In On Exactitude in Science, the writer Jorge Luis Borges imagines an empire so devoted to cartography that its mapmakers draw a map as large and detailed as the empire itself. “In the Deserts of the West, still today, there are Tattered Ruins of that Map,” Borges writes, “inhabited by Animals and Beggars.” Borges’s map is a parable for knowledge, and one of its lessons is that too much detail can quickly become impractical — a map at that scale would be perfect but useless.

But with today’s AI systems, one might wonder if such a map is so absurd after all. Computers and the Internet have already helped us to digitize much of human knowledge, and AI enables us to scan it quickly and easily. For instance, large language models are trained on trillions of words spanning much of recorded human knowledge. In biology, systems like AlphaFold learn from large databases to predict a protein’s folded structure from its amino acid sequence.

This means that, in some domains, something resembling Borges’s life-sized map has become extremely useful. And given the rate of progress on this front, it may seem like advancing science now simply requires building ever larger and more navigable versions of such AI systems, effectively mapping every field.

A lack of practicality, however, was never the sole flaw of Borges’s map. The deeper problem is that adding detail only gives you more of the same kind of information — more roads, more mountains, more villages — when what you might need is a completely different schematic.

Consider the map of the London Underground. Until 1933, the map plotted stations at geographically accurate locations in London. But this made central London, where most stations clustered, an unreadable tangle, while the outer suburbs, devoid of relevant data, took up most of the space. The draughtsman Harry Beck solved this inefficiency by abandoning geographic accuracy and instead redrawing the network as a circuit diagram of colored lines and evenly spaced stations.

A scientific paradigm can also be thought of as a kind of map, but unlike Beck, scientists do not usually know in advance what their maps will be used for. Instead, new paradigms are driven by the desire to explain complex phenomena with a simple and unified set of principles. Such principles tend to have knock-on implications that stretch far beyond the phenomena that inspired them.

For instance, by the mid-nineteenth century, electricity and magnetism were described by a patchwork of separately discovered laws, each explaining a different phenomenon. The physicist James Clerk Maxwell simplified the field by replacing this patchwork with four short equations. But they also implied the existence of electromagnetic waves that could travel through space, including low-frequency waves no one had yet detected. These waves eventually became the basis for radio.

Current AI, by contrast, is not set up to do this. It excels at prediction within existing frameworks, but paradigm shifts require replacing these with simpler alternatives whose implications haven’t yet been explored. A computational system trained on electromagnetic measurements may have predicted these results perfectly, but would never have found radio.

Seen in that light, even as AI becomes more central to scientific work, we risk falling into what one might call hypernormal science, where we get ever better at prediction within current models, alongside a weakening capacity to ask completely new categories of questions. Much like Borges’s empire of cartographers, we risk confusing more detail for a true understanding of the territory.

To avoid this kind of myopia, we must deliberately build AI that helps us devise new conceptual vocabularies. In other words, we must build visionary machines rather than merely predictive ones.

How Paradigms Work

Before exploring how to build such visionary AI, it helps to look more closely at how paradigm shifts in science actually happen. Science usually progresses by adding facts within an existing paradigm, which functions like a rulebook for a field. But over time, evidence accumulates that an existing paradigm cannot explain, requiring a new one.

One might expect that a new paradigm would immediately replace the old one as it better explains the facts. Instead, they tend to gain preeminence only after becoming useful for new applications.

One example is the development of special relativity. In the late nineteenth century, physicists could describe light with wave equations. Because every familiar wave (like sound or water) seemed to need a material carrier, the scientific consensus was that light must also travel through an invisible medium, dubbed the luminiferous ether. The academic establishment was profoundly attached to this concept; Lord Kelvin, the elder statesman of British physics, even declared the ether was the only thing in physics we could be absolutely certain existed.

Albert A. Michelson and Edward W. Morley reasoned that if the ether existed, the Earth’s motion would create an “ether wind,” making light traveling along that wind move at a slightly different effective speed than light traveling across it. Michelson and Morley sent light along two perpendicular paths and expected that because of this speed difference, one beam would come back slightly later than the other. But their experiment revealed no detectable difference.

This result didn’t immediately convince the academic community to abandon the concept of ether. Many physicists (including Michelson) instead adopted an interim position, that the ether’s effects must be hidden in some way. Most prominently, Hendrik Lorentz proposed that the ether existed, but that objects moving through it would shorten in the direction of travel, canceling the expected signal.

An alternative paradigm was ultimately offered by Albert Einstein, then a 26-year-old patent clerk in Bern, Switzerland. His theory of special relativity posited two principles: that the laws of physics are the same in every uniformly moving frame, and the speed of light in a vacuum is the same for all such observers. Through these principles, Einstein was attempting to introduce “a simple and consistent theory,” by which “the introduction of a ‘luminiferous ether’ will prove to be superfluous.”

Initially, Lorentz’s and Einstein’s theories both explained the known experimental data similarly well. But Einstein’s theory proved far more fruitful over time. If light’s speed were genuinely constant, then space and time could not be absolute. This eventually led to the demonstration that mass and energy had to be equivalent, as per Einstein’s famous equation, E=mc², which now underpins technologies from nuclear power to medical imaging.

A paradigm can take hold even if incomplete, provided its core idea is sufficiently useful. For instance, Charles Darwin’s theory of natural selection offered a single principle that could explain the diversity of living species even though it still lacked an explanation for how traits actually passed from parent to offspring. In the late 1860s, he posited the missing mechanism, the erroneous notion of “pangenesis.” In it, he speculated that every cell in the body sheds tiny particles called “gemmules” that collect in the reproductive organs and transmit traits to offspring. Despite this error, Darwin’s core vision survived, and spread amongst biologists, before genetics supplied the necessary, physical mechanisms.

Thus, Einstein and Darwin were both able to generate simple and elegant theories that could make predictions beyond current evidence, even when some details were missing or wrong. In both cases, their decisive advantage was not technical skill within the paradigm, but rather a willingness to step outside it: Einstein benefited from being an outsider to the academic establishment, as this freed him from attachment to the idea of the ether,1 while Darwin appropriated concepts from Charles Lyell’s geology and resource competition from Thomas Malthus’s economics.

Current AI Training Risks Hypernormal Science

If paradigm shifts require stepping outside the prevailing logic, we should ask whether current AI is set up to do this.

Consider an early attempt. In the late 1970s, computer scientist Douglas Lenat built the Automated Mathematician, a program designed to discover not just new facts but entire mathematical concepts. It would start with simple ideas, combine and vary them, and keep the results that seemed interesting. It appeared to work, reportedly rediscovering prime numbers and Goldbach’s conjecture. But its creativity turned out to be limited, because many of the concepts it “discovered” were already implicit in the way mathematics was written inside the program.

While today’s AI has vastly more power than the Automated Mathematician, a similar constraint applies. Most machine-learning systems are trained by minimizing prediction error against a dataset whose inputs and labels are defined in advance. This makes them very good at predicting current data, but locks them into the conceptual vocabulary of the data they learn from.

Consider medicine before germ theory. In the mid-nineteenth century, doctors thought that illness was caused by noxious air, and kept meticulous records accordingly. The physician William Farr mapped cholera deaths across London and found they correlated strongly with low elevation, which he thought was because noxious vapors accumulated in low-lying areas. He was actually picking up a real signal: low-lying districts were closer to the contaminated Thames River. But because his data was organized around air quality, he could not find the true cause.

An AI trained on Farr’s records could have found even subtler correlations, and would have been genuinely useful for predicting which neighborhoods would be hit hardest in the next outbreak. But it would not be able to derive the concept of a waterborne microorganism, as this was not a variable anyone had yet recorded. It took researchers like Louis Pasteur and Robert Koch, working with microscopes and culture dishes rather than statistical registers, to establish germ theory and open the door to antibiotics, antiseptic surgery, and modern public health.

In 2023, Google DeepMind used a graph neural network called GNoME to predict the stability of crystal structures at an enormous scale, discovering 2.2 million new materials. But the vast majority were substitutions within already-known structure types, for instance swapping one element for a neighboring one on the periodic table. The system optimized impressively for thermodynamic stability relative to known structures, but could not venture far from these.

Some newer AI models, known as foundation models, sidestep this problem partly by learning directly from raw data rather than human-curated labels. For instance, the protein generation model ESM3 was trained on protein sequences and structures, and managed to design a novel fluorescent protein highly different from those found in nature.

While impressive, generating novel proteins in this way is analogous to filling in unexplored spaces on a map, but not to creating new maps entirely. ESM3 does not, for instance, ask whether an amino acid sequence is the right level of description, or whether some other organizing principle might unify protein behavior with phenomena outside biology.

When researchers trained a foundation model on ten million simulated solar systems, it learned to predict planetary orbits with high accuracy, but acquired no representation of gravity. Instead, it had assembled a patchwork of statistical regularities that happened to produce correct trajectories. Of course, it is possible that such models already contain, buried in their weights, patterns that point beyond current theories; but extracting them would require deliberate study in its own right.

This grows in importance as scientists use AI more often in their work. On the far end of this spectrum, researchers have begun to develop “AI scientists,” end-to-end pipelines that aim to execute the whole scientific workflow by chaining together literature search, idea generation, code writing, experiment execution, and paper drafting. If these systems are successful, they might be able to work much faster than human scientists, and thereby may constitute the majority of scientific work that gets done.

But these systems have to evaluate the quality of the new ideas they generate, and it is hard to do so without reference to the existing paradigm. When the system proposes a new hypothesis or experiment, the only available proxy for what constitutes a good idea is consistency with existing science. This often involves passing simulated peer review, aligning with established results, and looking like a plausible contribution to the field. A genuinely novel reframing would likely score poorly on all of these measures, for the same reasons that paradigm-shifting work has always faced resistance from reviewers trained in the paradigm it aims to replace.

Simply put, optimizing performance on extant benchmarks makes it difficult for alternatives to emerge. And this, in turn, risks hypernormal science.

Consider a thought experiment in genetics. For centuries, breeders kept detailed records of which animals were mated, what their offspring looked like, and which traits appeared in which family lines. An AI trained on such data could learn to predict what size, color, or yield the offspring of any given two parents might have, which would surely prove immensely useful.

But such a predictor would never discover the gene as a discrete unit of inheritance, nor DNA as its carrier. Without that insight, while farmers may have been thrilled with their better breeding predictions, we would not have had the ability to create genetically modified organisms or targeted gene therapies. Indeed, a prolonged state of hypernormal science is dangerous precisely because its practical implications would not be immediately obvious.

There are early indications that this is already happening. A recent study of 41 million research papers found that scientists using AI publish more and receive more citations, but collectively, AI-augmented research covers around five percent less topical ground. This appears to be because AI gravitates toward problems rich in existing data, where the current paradigm is most established. The result is that AI induces authors to converge on known solutions, rather than search for new ones.

The Bitter Lesson for Science

In a 2019 essay entitled The Bitter Lesson, the computer scientist Richard Sutton observed that methods which try to build in human knowledge consistently lose out, over time, to methods that simply scale search and learning. “We want AI agents that can discover like we can,” he writes, “not which contain what we have discovered.” This applies naturally to paradigm shifts, which by definition move beyond existing knowledge. It might seem, then, that the path to paradigm-shifting AI is to get out of the way and let computation run.

Indeed, open-ended systems like AlphaZero (which learned chess entirely through self-play) are capable of creating both powerful and highly original results. Starting from nothing but the rules, it played millions of games against itself, generating strategies and discarding the ones that lost. Within a day, it was playing at a superhuman level, and did so while playing extremely original moves. The grandmaster Peter Heine Nielsen compared it to a superior species landing on Earth and showing us how to play chess.

Science might seem like a more complex version of the same problem, requiring more powerful computation to solve. In some senses, though, the opposite is true. Chess has simple rules, but a winning strategy is extraordinarily complex. In science, the winning paradigms can be extraordinarily simple; special relativity only has two postulates. But without the benefit of hindsight, there is no clear way to pick a winning paradigm.

To design AI for disruptive science, we would need to understand what “rules” make one paradigm better than another, and build systems that optimize for these. This turns out to be a harder problem than scaling compute. The answer cannot simply be experimental success, since experiments are slow and do not always reliably distinguish between paradigms (as was the case with Lorentz and Einstein). And there are other plausible candidates, but none yet offer a sufficient formulation.

One rule might be that good paradigms are simple. There are early attempts to make AI optimize for this. For example, in physics, symbolic regression systems such as AI Feynman try to discover the simplest equation that explains the data, instead of doing a black-box mapping. On benchmarks drawn from the Feynman Lectures, the method discovered all 100 test equations, while prior software found only 71. One can even formalize a drive towards simple theories using the Minimum Description Length principle, which effectively penalizes unnecessary complexity.2

But these systems currently work on clean data with pre-selected variables, and only search one dataset at a time. So far, they have been tested on rediscovering equations we already know, but haven’t yet demonstrated that they can find new ones.

Another rule may be that good paradigms draw effective analogies. Feynman devoted a chapter of his Lectures to the observation that heat flow, fluid flow, diffusion, and electrostatics all share the same equations, treating this as a deep fact about nature. This makes intuitive sense: an idea that already works in two domains has a better chance of working in a third.

The most obvious kind of analogy is across disciplines, as when Darwin borrowed the logic of competitive scarcity from economics and applied it to biology. In principle, AI could search for these connections at a scale no individual researcher could match, trawling across fields for ideas that seem structurally similar. Early systems have been built that find functional analogies across large databases of patents and product descriptions.

But some analogies are not between written theories, but rather between an idea and a sensory intuition. At sixteen, Einstein imagined riding alongside a beam of light and asked what he would see. Maxwell’s equations modelled light as a wave. But if this were true, if one travelled at the speed of light, the wave would appear frozen, hanging motionless in space. To Einstein, this picture felt physically wrong; this visceral discomfort ultimately inspired him to develop special relativity.3

Some research programs are trying to ground AI reasoning in physical experience. There are early attempts at multimodal architectures that can jointly process vision, language, and action. Self-driving laboratories couple AI to robotic instruments that manipulate real materials, which could in principle ground abstract reasoning in physical feedback (though most operate within a single experimental domain). But these are early efforts, and the gap between a robotic arm pipetting reagents and multisensory human experience is vast.

In the meantime, the fastest path to getting effective analogies may be leveraging both human and AI abilities together. Humans have breadth across modes — we see, hear, touch, move through space, and read, all at once — which grounds our capacity for structural analogy. AI has depth within modes, having processed far more than any person ever could. If AI can help researchers learn faster across disciplinary boundaries, perhaps by disciplined use of LLMs, that alone could accelerate discovery.

The deeper problem is that we do not have a good formal understanding of how paradigm shifts actually happen. Simplicity and analogy alone do not appear to be a complete description. J.J. Thomson’s “plum pudding” model imagined atoms as spheres of positive charge with electrons scattered through them. It was simple, matched what was known at the time, and was comically analogical, but soon proved completely wrong.

For now, then, the Bitter Lesson for Science may be that scientific acceleration will not happen by default until we understand science itself better.4 But if we can identify the conditions that produce paradigm shifts, we can start to engineer them.

A Paean for Metascience

Understanding and codifying science is no small task. Since Bacon’s Novum Organum in 1620, we have had a reasonable account of how science works in theory — observe, form hypotheses, test, and revise. But paradigm shifts seem to depend just as much on conditions as on method: who gets to do science, what they are rewarded for, and how freely ideas can cross between fields, for instance.

We can learn some things from history. Bell Labs, Xerox PARC, and the early Laboratory of Molecular Biology at Cambridge all produced extraordinary concentrations of paradigm-shifting work, mostly because they were small groups with enough institutional protection to pursue ideas that looked unproductive by conventional measures. There are clear parallels, in fact, to the kind of independent self-play that made AlphaZero successful. But there are limited numbers of historical paradigm shifts to study, and we have barely begun to explore the design space.

Here, AI itself may be able to help. We have never been able to run controlled experiments on scientific institutions; it is impossible to create labs that differ in only one respect and compare the results. But we could run AI agents in parallel populations under different research conditions, and analyze the results in detail. In this sense, AI scientists may give metascience its first model organism.

For instance, one could test how group structure shapes discovery: do small, isolated teams produce more conceptual reorganization than large, well-connected ones? Do flat hierarchies outperform rigid ones? One could run AI agent populations that vary these factors independently and measure the results — something that is impractical to do with real institutions, where size, hierarchy, and communication patterns are all entangled.

Some of the optimism around AI for science rests on the intuition that if we build systems with much stronger general reasoning, discovery will follow as a near-automatic consequence. But there is no guarantee that this will happen by default. Many technologies have promised radical scientific acceleration, and so far, not completely fulfilled their promise.

The Internet, for example, made knowledge much easier to search, and in theory may have led to much faster science. Online collaboration has certainly sometimes enabled better scientific work, such as in the Polymath Project. But this revolution has largely not emerged at scale, mostly because deeper inefficiencies in how we organize science (e.g., career incentives) remain a bottleneck. There is even evidence that online journals actually narrowed what researchers read and cite, because scientists search or follow hyperlinks rather than browsing journals, thus potentially accelerating consensus rather than expanding the space of ideas explored.

AI could repeat this pattern at a larger scale — generating faster results within the existing paradigm, while the structural conditions for disruptive science remain unchanged or worsen. There is no reason to expect this design problem to sort itself out on its own. But if we treat AI for disruptive science as a deliberate research program, we have a better chance of building the capabilities that paradigm shifts require. And to do that, we will have to understand how to design science itself.

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Alvin Djajadikerta is the CEO of Evidentia Labs and a founding researcher at Science Works. He holds a PhD in Molecular Neuroscience from the University of Cambridge.

Cite: Djajadikerta, Alvin. “Designing AI for Disruptive Science.” Asimov Press (2026). DOI: 10.62211/29ej-27et

By Rachel Dutton

The human immune system is, in one sense, a detection mechanism. It has evolved, over millions of years, to scan the body for molecular signals that tell it whether to attack or stand down. Most of these signals come from pathogens, damaged cells, or the body’s own hormones. But in 2019, a lab in Germany published a finding that pointed to a much stranger source: one of the signals sensed by the immune system is found in sauerkraut.

When people eat sauerkraut, a molecule called phenyllactic acid (D-PLA) — found in fermented foods — enters their bloodstream and activates a receptor, known as HCA3, on immune cells, triggering an anti-inflammatory response. In addition to lactic acid, phenyllactic acid is one of many compounds produced by lactic acid bacteria during the fermentation of sauerkraut and related fermented foods. Prior to this study, other molecules had been found to bind HCA3, but D-PLA was a hundredfold more potent than any of them.

This discovery advances our understanding of how fermented foods can reduce inflammation and positively affect human health. But more striking is what it suggests about hominid physiology. Although HCA3 is part of a larger family of receptors broadly conserved across eukaryotes, HCA3 is only present in humans and other great apes like chimpanzees and gorillas — and not even in other mammals. It is a recent addition to the genome, appearing only a few million years ago. Its existence seems to suggest that our immune system evolved to recognize the microbial metabolites from fermented foods.

We tend to think of fermented foods as something humans invented and then chose to eat. But, increasingly, scientific evidence suggests the causality runs the other way. Fermented foods appear to have helped shape human biology itself, and our bodies may have been built, in part, to expect them. The case for this runs from changes in hominid gut anatomy millions of years ago to the HCA3 receptor, to a growing body of research linking fermented food consumption to immune function and gut health. And it raises an uncomfortable question about what happened when the Western food system, in the name of safety and efficiency, quietly removed these foods from our diets in the nineteenth and twentieth centuries.

Early Fermentation

Fermented foods are the result of the controlled growth of communities of microbes. At their core, they are the products of the interaction of these microbes and whatever food they consume, whether cabbage or cucumber. While this process varies from food to food, fermentation typically involves managing environmental variables such as oxygen, temperature, and salinity. In contrast to food preservation methods like canning or even pickling, which are designed to prevent microbial growth, fermentation harnesses the capacity of naturally occurring microbes found on fresh food or in the environment to outcompete spoilage organisms.

Most archaeological evidence from pottery shards suggests that fermented food production is at least 7,000 to 10,000 years old. This timeframe coincides with the major transition to agrarian lifestyles, which would have reliably produced surpluses of food and the subsequent need for preservation methods.1 While this explanation satisfies most scholars, there is reason to believe that fermentation may be far older.

For one, it’s a very simple process to trigger. Some foods even ferment spontaneously. In the case of alcoholic drinks, like beer, wine, or mead, ubiquitous yeast species, which are naturally found on grapes and other fruit skins, rapidly use sugar as a food source for reproduction, producing ethanol as a byproduct. The same results occur when ripe fruit falls to the ground and its sugar is exposed to the environment, or when honey is diluted with water.

Other processes require only minimal intervention. For example, submerging fresh food in liquid or burying it creates a low-oxygen environment that encourages the growth of acid-producing bacteria that preserve the food by what is called “lactic acid fermentation.” This technique produces dill pickles, sauerkraut, and kimchi. While salt is often added as an additional intervention against unwanted microbes, it’s not required as it isn’t the primary driver of the fermentation.

Another argument for an earlier origin for fermented foods is that they are found across nearly all human cultures. While the number of fermented foods in the modern, Western diet is fairly limited (cheese, yogurt, bread, chocolate, coffee, beer, wine, kimchi, and kombucha) hundreds more are eaten around the world, from fermented shark in Greenland to a seemingly limitless variety of fermented soy beans in Asia. This diversity is a testament to how humans gradually mastered this ancient practice and modified it to suit new environments as they moved out of Africa.

Around 14 million years ago, our hominid ancestors were arboreal species whose diet would have been primarily based on fresh fruits picked from the trees they lived in. When ripe fruit fell to the ground and underwent spontaneous fermentation, it would have been toxic to our ancient ancestors due to its high concentration of ethanol. Their bodies as yet had no efficient way to break down ethanol.

But then, about 10 million years ago, a mutation arose in the genome of the common ancestor of humans, gorillas, and chimpanzees. This mutation, a single amino acid change in the enzyme Alcohol Dehydrogenase 4 (ADH4), enabled it to break down and detoxify ethanol with 40x higher efficiency. The capacity to consume this energy-rich but previously dangerous fruit may even have driven our transition from an arboreal lifestyle to a terrestrial one. What’s more, this ability to tolerate ethanol may have been what allowed our ancestors to diversify their diet and survive while lineages without this mutation went extinct.

The fossil record shows that a major shift in hominid anatomy occurred around 2 million years ago, when hominids developed a smaller rib cage and larger skull. At the same time, another major change took place in their intestines. Compared to our closest relatives, humans have a digestive tract that is 40 percent shorter. This decrease was thought to be driven by the external processing of our food, which reduced the time and energy involved in chewing and digesting. Anthropologist Richard Wrangham argues that the technological innovations of controlling fire and cooking food led to this major change, and that the excess energy we got from cooked food, in turn, supported the evolution of a larger brain.

However, two recent studies, by biological anthropologist Katie Amato in 2021 and evolutionary biologist Erin Hecht in 2023, suggest that these anatomical changes may have been driven by human use of fermentation even before humans began to cook. By allowing microbial species to ferment and break down complex carbohydrates and other macromolecules in foods, we may have turned over certain parts of an otherwise energy-intensive digestive process to microbes in a form of “external digestion.” This use of fermentation to pre-digest food, intentional or not, may have served as a predecessor to cooking, providing the extra calories needed to support the evolution of a larger brain.

Another benefit of fermentation is that it offered access to foods which, previously, would have been toxic. As our ancestors came down from the trees and needed new ways to fill their stomachs, the tubers of many plants and grasses offered an appealing, ready source of calories. Tubers contain large deposits of starch. Root vegetables, such as potatoes, yams, and carrots, are our modern-day, highly domesticated equivalents. But the wild tubers of our ancestors’ time were hard to chew, and some contained low levels of toxins. Varieties of cassava, for example, contain compounds that release cyanide when ingested. After just a few days of fermentation, however, microbes destroy these dangerous molecules and make the food safe to eat.2

Ultimately, given the simplicity of the fermentation process, its provision of new food sources, and its role in decreasing the need for extensive chewing and digestion, fermentation could have had an outsized impact on human evolution. It may, in fact, have helped make us human.

Peril and Promise

Perhaps the most striking thing about fermentation is that humans figured out how to control the growth of microbial species long before we understood what “microbes” were.

No one had seen microbial life until the 17th century, when Dutch scientist Antonie Van Leeuwenhoek used a handmade microscope to reveal small, motile forms he described as “animalcules.” It wasn’t until the late 1800s, however, that the French chemist Louis Pasteur demonstrated the role of microbes through his studies of fermented foods. His work on the spoilage of beer and wine formed the basis of the “germ theory” of disease. If microbes could be the causative agents of spoilage in food, Pasteur reasoned, maybe they could also be the causative agents of disease.

For his part, Pasteur was not strictly “anti-microbe.” He found them enthralling, investigating the differences between lactic fermentation (yogurt, pickles, and sauerkraut), butyric fermentation (butter, cheese, and milk), and acetic fermentation (kombucha, sourdough, sour beer), as well as developing the categories “aerobic” and “anaerobic” (which refer to whether microbes require oxygen to survive).

Even so, Pasteur’s work identifying microbes responsible for putrescence and disease has had the greatest impact on our food system. At the beginning of the twentieth century, automated machinery expanded canning capacity from roughly 10 cans a day to 1,000. Variation in the quality of the sealed lids, temperature treatments, and exposure to contaminants through handling meant a greater potential for microbial illnesses like botulism.

After three deadly botulism outbreaks in 1919 linked to California-distributed olives, the canning industry turned to Pasteur-inspired “bacteriologists” to design better canning systems and restore public confidence. While the resulting practices — including steam sterilization, the marking of batches, and traceable can coding — were at first voluntary, the Cannery Act of 1925 mandated statewide compliance.

By the mid-1900s, microbial research into food had come to focus on how to keep organisms out of it. Innovations in heat, pressure, refrigeration and anti-microbial agents to extend shelf life and decrease potential contamination with food-borne pathogens formed the core of academic and industrial research. As our methods of food production shifted, so did our diets. Americans largely moved away from the consumption of traditionally fermented foods, with one major exception.

That exception began with a single lecture. The Russian zoologist, Ilya Mechnikoff, based at the Pasteur Institute in Paris, was well known in the early 1900s for his scientific discoveries involving the immune system, for which he would win the Nobel Prize. But towards the end of his career, Metchnikoff became fascinated with the idea that aging was just another disease awaiting a cure.

In his 1908 book, The Prolongation of Life, Metchnikoff proposed that this disease was caused by "putrefying" microbes that lived within the human gut, or, as he put it, “chronic poisoning from an abundant intestinal flora.” His suggested cure came in an unexpected form — yogurt. Mechnikoff reasoned that just as the acid in sour milk prevented the growth of spoilage organisms, it might limit the growth of “spoilage” microbes in the gut.

After speaking with a student after one lecture, Metchnikoff learned of large numbers of centenarians in Bulgaria (one of whom he credulously reported as being “158” years of age).3 Metchnikoff hypothesized that the consumption of large quantities of yogurt in Bulgaria prevented aging through the action of lactic acid on gut bacteria. After obtaining a sample of the “Bulgarian bacillus” (Lactobacillus delbrückii subsp. bulgaricus) from yogurt, he set out to study the effects on the gut. His lab work showed that the presence of the yogurt microbe and the lactic acid it produced slowed the growth of intestinal microbes.

Metchnikoff thus advised the consumption of yogurt to promote healthy intestinal balance, writing: “A reader who has little knowledge of such matters may be surprised by my recommendation to absorb large quantities of microbes, as the general belief is that microbes are all harmful. This belief, however, is erroneous. There are many useful microbes, amongst which the lactic bacilli have an honourable place.”

Metchnikoff initially presented his yogurt hypothesis at a public lecture in 1904 in Paris, titled “Old Age.” The lecture went the early 1900s equivalent of viral. Newspapers ran stories with headlines like “Drink Sour Milk and Live to be 180 Years Old” (Evansville Courier and Press) and “Sour Milk is Elixir: Secret of Long Life is Discovered by Prof. Metchnikoff” (Chicago Daily Tribune). “Within months of Metchnikoff’s lecture, milk-souring germs had blossomed into an international business. Pharmacies throughout Europe and the United States were offering Bulgarian cultures in the form of tablets, powders, and bouillons — to be consumed as is or used,” writes Luba Vikhanski in her book Immunity. It was, in effect, the first “superfood.”4

“Probiotic” products quickly followed, containing dehydrated “lactic bacilli,” that anyone could use to sour their own milk in the way prescribed by Metchnikoff. But despite interest in yogurt and probiotics as health foods, most 20th century microbiologists remained focused on “bad actors,” the microbes and pathogens involved in disease. However, this changed toward the end of the century with advances in sequencing technology and chemical analysis techniques like mass spectrometry, which allowed them to probe microbial genetics and metabolism more closely and with more nuance.5

Environmental DNA sequencing revealed the diversity of microbial species across habitats, including in and on the human body as well as in our food. Understanding what these microbes are doing, and how, has become one of the challenges of modern microbiology.

To Eat Microbes

In response to this challenge, a lab at Stanford University, led by Erica and Justin Sonnenburg, has been doing seminal work on the human gut microbiome and how species within it function and interact. Recently, the Sonnenburgs have turned their focus on diet-microbiome interactions to fermented foods. A clinical trial, which the Sonnenburgs set up in collaboration with nutrition scientist Christopher Gardner in 2021, offered the clearest evidence to date that fermented foods are essential for gut health. In the trial, 36 healthy adults spent 10 weeks eating a diet high in such foods.

At the end of the study, they showed increases in gut microbiome diversity, which is generally associated with gut health. (The participants had new microbial species in their guts, which did not come from the fermented foods. It seems, rather, that fermented foods somehow make the existing gut ecosystem more receptive to incorporating new strains.) Perhaps an even more impactful outcome was that the researchers also found widespread decreases in inflammatory markers in the blood of these participants.

Given that low levels of inflammation sustained over time, referred to as chronic inflammation, is believed to be implicated in many diseases, the ability to decrease it though simple dietary changes would be welcome. However, the six servings of fermented foods a day consumed by the study participants is far higher than that in most U.S. diets. While yogurt and cheese are commonplace, with an average of 13.8lbs and 42.3lbs consumed per person per year respectively, this represents about a serving of fermented dairy a day. Fermented vegetables also comprise less than a serving per day. The impressive 387 million pounds of sauerkraut Americans consume per year equates to only 1.5lb per person, or about 0.06 servings a day.6 There has been a resurgence in interest in fermented foods, from high-end chefs experimenting with new types of fermentations to home fermenters caught up in the pandemic sourdough craze, but we have a long way to go before consumption reaches levels needed for clinically meaningful outcomes.

Even larger gaps remain in our understanding of how fermented foods actually drive health benefits. Beyond inflammation, fermented food consumption has been associated with a wide range of positive health outcomes, from gut health to mental health. As compelling as the Sonnenburg study is, it doesn’t yet reveal the mechanism(s) by which fermented foods trigger changes in human physiology.

While the 2019 sauerkraut study points to the importance of microbial metabolites like phenyllactic acid, if we co-evolved with fermented foods over millions of years, this example of a metabolite-receptor pairing is likely just the tip of the iceberg. As in many other areas of microbiome research, we need to move beyond correlation to causation. Doing so will require a much deeper understanding of the molecular composition of fermented foods, how they are connected to human biology, and more precise clinical studies.

Scientists are beginning to recognize the potential diversity of bioactive metabolites in fermented foods, but most studies focus on a single food type at a time and use different assays of bioactivity from lab to lab. To be able to effectively map the complex interactions between fermented food microbes, metabolites, and human biology, we need larger, consolidated datasets.

To this end, the Microcosm Foods project has been assembling a first of its kind collection of fermented food data pairing metagenomics (mapping microbes), metabolomics (mapping metabolites), and transcriptomics (mapping changes in human immune cells upon exposure to fermented foods) across over 100 different foods. Open-source, systematically-acquired datasets such as these will help build the scientific foundation needed to untangle these complex interactions.

For most of human history, people harnessed microbial ecosystems to make fermented foods and reaped the benefits without understanding their mechanism. Then, in a period of roughly 100 years, the Western food system replaced them with sterile, shelf-stable alternatives.

Today, we are finally beginning to understand how fermented foods interact with our biology — through receptors like HCA3, through shifts in gut microbial diversity, and through inflammation pathways. Science is catching up to what fermentation has been doing all along.

Rachel Dutton is a microbiologist studying fermented foods, from their use as microbiome models to their impacts on health. She received a PhD in Microbiology and Molecular Genetics from Harvard University, and led academic labs at Harvard and UC San Diego. Rachel is currently a Resident at the Astera Institute and a Fellow in the Big If True Science program at Renaissance Philanthropy.

Credit: L. reuteri image by Anastasiia Dmytriv.

Cite: Dutton, R. “Culture Shift.” Asimov Press (2026). DOI: 10.62211/92yr-34qw

By Dr. David S. Kim

Researchers have known that the pancreas secretes several peptide hormones critical to metabolic regulation, most notably insulin and glucagon, since the early 1900s. With the advent of recombinant peptide synthesis in the 1970s, scientists not only began working on isolating the gene responsible for insulin production but fabricating it outside the body. In 1978, scientists at Genentech turned bacteria into factories able to transform sugar into insulin by cutting the insulin gene from the human genome and pasting it into the genome of E. coli. This breakthrough allowed peptide drugs to be synthesized at mass scale, without needing to be harvested from animal pancreases, and gave birth to the biotechnology industry.

The role of glucagon and the gene encoding it, however, remained elusive. Then, in 1982, Joel Habener and colleagues at Massachusetts General Hospital (MGH) published a paper indicating not only that they had located the human glucagon gene, but that it actually encoded three separate peptides, two previously unknown. Those two unknowns were labelled as glucagon-like peptides: GLP-1 and GLP-2.

Svetlana Mojsov, a peptide chemist also working at MGH, managed to synthesize a truncated, but active, form of GLP-1. In 1987, her paper with Habener and Daniel Drucker showed that GLP-1 stimulates glucose-dependent insulin secretion in the pancreas, suppresses glucagon release, and slows gastric emptying, all of which stabilize blood sugar levels after eating.

While these effects initially made GLP-1 seem a promising candidate for drug development, the earliest clinical studies from 1992 and 1993 revealed that GLP-1’s half-life in the body was disappointingly short. A proteolytic enzyme, dipeptidyl peptidase-4 (DPP-4), binds to and destroys GLP-1 molecules in the blood in minutes.

Hope for boosting GLP-1’s half-life in the body came in the 1990s, when endocrinologist John Eng, at the Bronx Veteran Affairs Hospital, noticed something curious about the Gila monster while researching snake and lizard venom effects on the pancreas. Specifically, he was struck by how this desert lizard eats extremely infrequently, yet somehow maintains a stable blood sugar level for months.

Eng found that Gila monsters secreted a salivary venom peptide, now known as exendin-4. Structurally similar to GLP-1 but unaffected by DPP-4, this peptide lingers in the blood for hours rather than minutes. Exendin-4 thus became the molecular blueprint for exenatide, the first twice-daily injectable GLP-1 receptor agonist, approved by the FDA in 2005.

For many years after exenatide’s approval, GLP-1 receptor agonists were used primarily as diabetes medications. Practitioners and patients noticed, however, that taking such medicines produced weight loss as a side effect. During this time, researchers also found GLP-1 receptors in the brain and pancreas, particularly in areas controlling appetite and reward. And in 2021, the results from a series of five STEP trials (Semaglutide Treatment Effect in People with obesity) demonstrated marked weight loss even in individuals without type 2 diabetes (T2DM): Phase 3, for example, showed an average loss of about 15 percent over 68 weeks, more than double achieved by any prior obesity drug. In 2023, a trial of 17,604 adults (SELECT) with obesity and without T2DM, followed for over three years, showed a 20 percent reduction in major adverse cardiovascular events.

In response, GLP-1 prescriptions rose sharply. According to CDC data, the share of adults with type 2 diabetes using GLP-1 injectables more than doubled — rising 155 percent between 2018 and 2022 — while overall spending on these medications climbed more than 500 percent between 2018 and 2023.

The majority of patients continue to inject these drugs rather than take them orally. But a 2020 survey of 600 patients found that 76.5 percent would prefer a once‑daily oral dose over a once-weekly injection of GLP-1. Significant funding is going into R&D to launch an oral alternative that performs as well as an injectable version. While oral formulations are beginning to enter the market, so far they remain less effective and more expensive to manufacture. Why?

To the Stomach, All Peptides Are Food

Peptide drugs like GLP-1s are made up of a chain of amino acids chemically bonded together. For a GLP-1 molecule taken by mouth to reach its target, it must first pass through the stomach, where hydrochloric acid and peptidase enzymes cleave these amino acid bonds. Most ingested peptides are simply broken down into their constituent amino acids and absorbed as nutrition, indistinguishable from the protein in food.

The small percentage of GLP-1 molecules that might survive this journey and arrive into the intestines face a second gauntlet. Once in the blood capillaries, DPP-4 quickly degrades the molecule, and the drug is excreted by the kidneys.

Biochemical engineering, however, has allowed drugs like semaglutide to survive longer in the blood. First, an amino acid substitution stops DPP-4 from destroying GLP-1. This is achieved by swapping the alanine amino acid at position 8 in the peptide backbone for alpha-aminoisobutyric acid (Aib), a modified amino acid that DPP-4 cannot recognize or cleave. As a result, this modified form of GLP-1 is not degraded so swiftly.

Yet even a DPP-4-resistant peptide is small enough to be filtered by the glomeruli in the kidneys into the urine. Therefore, the chemists behind semaglutide made a second modification: they fused a fatty acid chain to the peptide in a process called lipidation. This causes the drug to bind to human serum albumin, a large transport protein abundant in the blood, with a natural half-life of approximately 20 days. The drug effectively co-opts albumin’s stability and longevity; the lipidated GLP-1 molecules are bound to albumin, which is too large to be renally filtered, and are thus shielded from plasma proteases.

The combined effect of these modifications increase the drug’s half-life from minutes to approximately 168 hours, enabling its once-weekly injection schedule — an enormous improvement compared to the twice daily injection required for exenatide (Byetta) which was the first GLP-1 drug that was launched.1 Semaglutide (under the brand names Ozempic and Wegovy) swept the market. However, these modifications to the molecule could not solve the problem of degradation and poor absorption when taken by mouth.

From Silkworm to Trojan Horse

We might draw parallels for oral delivery of peptide and protein drugs from the case of serratiopeptidase, a little‑known drug from the 1960s with a peculiar history.

Serratiopeptidase is used to treat post‑operative inflammation in a handful of countries, including Japan, India and Sierra Leone. Produced naturally by the bacterium Serratia marcescens, which resides in the gut of the Japanese silkworm, this enzyme is used by the moth to dissolve silk fibers as it emerges from a cocoon. It is pharmacokinetically puzzling as an oral therapy because, as a peptide, it faces the usual hurdles of gastric degradation and poor epithelial uptake. Yet, surprisingly, no injectable formulation of serratiopeptidase is marketed. The reason is that intravenous administration carries a risk of immunogenicity — the immune system recognizes Serratia‑derived molecular signatures on the enzyme as foreign, which can trigger immune reactions. This danger is blunted or even absent, however, when the drug is given orally.

Serratiopeptidase only works because the oral dose is high enough that the small fraction of the drug which survives the gut reaches systemic circulation at concentrations sufficient for therapeutic effect. In this way, it serves as a proof‑of‑concept that even a peptide or protein drug known to have poor bioavailability can still be delivered orally, and without any modification, if we compensate by delivering a sufficiently high dose.

But in general, turning a peptide (including GLP-1 or insulin) into an oral formulation means overcoming three major challenges: protecting the peptide from digestion in the stomach, improving absorption of the peptide via the gut, and slowing down the enzymatic breakdown and excretion of the peptide once it is in the blood. Novo Nordisk’s oral semaglutide, Rybelsus, employs both co-formulation and clever biochemical engineering of the drug molecule itself to move us closer to this goal.

Specifically, Rybelsus works by co-formulating semaglutide with SNAC (sodium N-[8-(2-hydroxybenzoyl) amino] caprylate), a small synthetic molecule that functions as an absorption enhancer in the gastrointestinal tract. SNAC raises the pH of the immediate environment around the drug. The higher pH protects the peptide from pepsin degradation, which requires acidic conditions. SNAC also acts as a transient permeation enhancer, aiding semaglutide’s absorption into the blood, directly through the stomach lining and the small intestine.

While this co-formulation certainly improves oral delivery, it hasn’t fully solved the problem of dosage requirements. One pharmacokinetic study showed a modest bioavailability of only 0.8 percent for oral semaglutide, meaning less than one percent of the drug is absorbed into the blood where it can take effect.

To be effective, then, Rybelsus must be formulated to contain high doses of semaglutide. Whereas the GLP-1 drug Ozempic is injected once weekly at 2 mg, Rybelsus is taken daily and requires a minimum dose of 14 mg to achieve comparable glycemic effects. That is almost a 50-fold difference in total weekly intake for what is, fundamentally, the same drug, simply because most of the substance is degraded before they can be absorbed into the blood.

Additionally, Rybelsus doesn’t perform as well as its injectable counterpart, even at this higher dosage. In clinical trials, Ozempic (2 mg weekly subcutaneous) delivered a 15-20 percent body weight reduction over 68 weeks. Rybelsus at the approved 14 mg daily dose, though, achieved just 4-5 percent in the PIONEER trials. However, at 50 mg, oral semaglutide (OASIS 1) narrowed that gap substantially, achieving 15.1 percent weight loss at 68 weeks, approaching injectable performance.

While it is no secret that the cost of production of the drug molecule itself is only a small part of the retail price, the higher dosage required by oral delivery becomes a non-trivial difference in manufacturing costs.

Semaglutide costs $70,000 to $100,000 per kilogram to manufacture at commercial scale, according to two studies. Producing the drug ingredient contributes only $0.20 to the cost of each weekly 2mg injection. What forms the bulk of the retail price2 of peptides is not the cost of manufacturing, but the capital infrastructure: the regulatory burden, the cold chain logistics, the pen device (which sometimes costs more than the drug itself), and, above all, the return needed to justify $9 billion in the initial R&D of these GLP-1 drugs.

The cost breakdown looks much different for an oral semaglutide. In the OASIS 1 trial, patients took a 50 mg daily dose — meaning a monthly supply contains roughly 1,500 mg of active drug compound. A monthly injectable supply, by comparison, contains only about 8 mg. At $100,000 per kilogram, the drug compound alone for an oral monthly supply could already cost around $150, versus less than $1 for the injectable — before factoring in formulation, packaging, distribution, or profit.

This is the central problem with oral GLP-1s, then; biochemical engineering can technically solve the half-life problem, and co-formulations can improve the absorption problem, but the higher doses required make for formidable raw ingredient costs.3

Turning Food into Drug Delivery Vehicles

A solution to this problem may come from foregoing chemistry and turning, instead, to biology.

Genentech pioneered recombinant manufacturing of human insulin by cloning the human gene into E. coli as far back as 1978. Even today, many GLP-1 peptides are made by cloning the corresponding gene into microbes, culturing them in a fermenter, and then subjecting the resulting broth to successive rounds of filtration and chromatography to isolate the peptide precursor before undergoing chemical modifications. E. coli, though, is not edible, as it is laden with endotoxins that can trigger a septic shock. Therefore, any drug made in a cell like E. coli must be purified extensively, even if delivered orally. This downstream purification accounts for up to 80 percent of the total manufacturing cost.

Suppose, instead, that the microbes used for production were also edible. The drug could then be swallowed inside intact cells, and the massive cost of purification would disappear. In theory, there are millions of microbe species that can be engineered to synthesize peptides. But currently, we have the tools to genetically engineer only a few, and most microbes have never been studied for food safety and toxicology.

One attractive candidate is the edible, single-celled cyanobacterium Arthrospira platensis (spirulina). Cyanobacteria and many microalgae species have been consumed by humans for centuries and are Generally Recognized As Safe (GRAS) by regulatory agencies. Many people already eat spirulina for its antioxidants. Thus, the organism could be quite appealing for direct oral delivery in its intact cellular form, if it could be engineered to synthesize a GLP-1 molecule in sufficient quantities. Given the low cost of production, a 20-gram scoop of dried “algae powder” taken twice daily could, in principle, contain an orally adjusted therapeutic dose of a GLP-1 agonist for around $4/day.4

The cost argument alone is compelling, but using edible algae provides another benefit: keeping the GLP-1 inside the algal cell wall may improve the drug’s survival in the gut. Experimental data have already demonstrated that over 70 percent of the expressed proteins in spirulina remained intact after two hours of incubation under simulated gastric conditions that would fully degrade the same protein in a purified form within minutes. The cell wall acts as a natural enteric capsule, shielding the GLP-1 molecules from pepsin and the acid bath of the stomach, and releasing it progressively as it transitions into the higher-pH environment of the duodenum.

The reason this concept has not yet been tested in the context of GLP-1 is because, until very recently, it was not possible to engineer microalgae and cyanobacteria. Spirulina was, until a few years ago, considered genetically intractable because it has multiple copies of its genome and is resistant to standard transformation methods. In 2022, though, a paper reported successful engineering and high-level expression of therapeutic proteins in spirulina, with the encoded proteins accumulating to up to 15 percent of total dry biomass.

Today, newer organisms like UTEX 3222 (discovered in 2023 and also known as “Chonkus”) can double several times faster than spirulina and be engineered to express recombinant peptides. Some of these strains are quite simple to grow, needing just light and CO₂. Their adoption might not only make oral GLP-1s affordable, but also allow the mass production of customized peptides from photosynthesis — all inside edible cells.

Many cyanobacteria (and microalgae broadly) are safe to eat, though not every strain of cyanobacteria has a GRAS certification.5 Under the GRAS framework, an ingredient has to be demonstrated as safe either “through (1) scientific procedures or (2) in the case of a substance used in food prior to January 1, 1958, through experience based on common use in food.” For cyanobacteria to be used as a platform for oral GLP-1 delivery, either a GRAS organism like spirulina must serve as the host organism or, if choosing a different species, the manufacturer must prove with adequate in vivo trial data that it is safe to eat.

In addition, one must gain FDA approval by clinically demonstrating that the delivery of the microbe-encapsulated GLP-1 through this oral route leaves the drug molecule itself unchanged (with no post-translational modifications), that it has a similar pharmacokinetic profile to the reference molecule, and that it shows no adverse effects. Since this is a new delivery platform of existing drugs rather than a new drug, the regulatory bodies in many jurisdictions typically have alternative, shorter approval pathways available to drug sponsors that do not require the standard Phase I-III clinical trials for a new drug application.

A third argument for adopting edible organisms for GLP-1 delivery would be to increase global accessibility. Bangladesh, for example, ranks among the world’s top ten countries for T2DM patient burden, with a prevalence of 9.2 percent among adults. The disease currently impacts over eight million people, a number projected to grow to 15 million by 2045. Yet GLP-1 drugs are effectively absent from the formularies of Low and Middle Income Countries (LMICs). A 2024 study found that GLP-1 drugs can likely be manufactured more cheaply than their current market costs of, for example, $95 in Brazil, $115 in South Africa, and $353 in the United States.

Médecins Sans Frontières has called for Novo Nordisk and Eli Lilly to license their patents to generic manufacturers, noting that neither company has adopted pricing strategies for low-income markets. The surge in U.S. demand has also triggered global shortages that hinder the drug’s availability for essential diabetes care in LMICs. If we can provide alternative biomanufacturing capacity that slashes cost, turns injectables into safe oral, algae-encapsulated formulations, and eliminates the need for refrigeration, we may be able to ensure that patients in LMICs are no longer last in line for the latest and best therapeutics.

So far, three major problems have kept GLP-1 drugs injectable rather than oral: enzymatic degradation, poor bioavailability, and the sheer cost of manufacturing. Novo Nordisk's Rybelsus showed that transcellular gastric absorption, boosted with SNAC, can partially get around the first two problems, but cannot solve the third. This is why research groups around the world are trying to engineer microbes to act as edible drug factories. The idea is to skip the most expensive part of manufacturing, downstream purification, by keeping the expressed peptide locked inside the protective walls of edible cells.

The science of oral peptides, at this point, is no longer a mystery. We know oral peptide drugs can work. The harder question is whether patients will come to accept the idea of eating their medicine in a spoonful of algae.

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David S. Kim is the founder of CyanoCapture [General Bio], a synthetic biology company that is manufacturing peptides by genetically engineering non-model microbes. He is a medical doctor based in the U.K.

Cite: Kim, D.S. “The Quest for Oral GLP-1s.” Asimov Press (2026). DOI: 10.62211/82ej-91yt

Living organisms are surprisingly creative when it comes to finding their way into hostile environments. Microbes, after all, thrive everywhere from hyperarid deserts and hydrothermal vents to the stratosphere.

Of all hostile environments, one might think the most unbreachable to be the laboratory, where populations of bacteria are stored inside tubes sealed with tight screw-caps and stacked in freezers at -80°C. Of course, normal evolutionary processes don’t magically stop at the doors of the lab: organisms still mutate, fragile microbial species can still be out-competed by faster-growing contaminants, and parasites can still spread. However, vigilant scientists devote considerable effort to making sure containers hold what is written on their labels and, when in doubt, can sequence any part of a sample’s DNA, discarding or incinerating undesired specimens.

Still, interlopers persist. One organism that has been particularly successful at infiltrating microbiology research facilities is called Φ80. It is a bacteriophage, or virus that infects bacteria. Slowly but surely, Φ80 has been spreading. Researchers carry out experiments, make reproducible observations, and publish — usually without ever realizing that their samples have quietly been contaminated with this phage.

On occasion, hidden contaminations of Φ80 have led to paper retractions, with researchers discovering not only that their results are artifactual, but that they personally amplified the invasion and transmitted it elsewhere. In a 2017 paper, for example, scientists confessed that “beyond the confusion created by our erroneous interpretation of results obtained with Φ80-infected strains, we are worried that we have sent these strains to many research groups.”

To understand how such unwitting contamination can occur despite researchers’ best efforts, and to work towards better containment, it helps to first understand how bacteria are typically cultivated.

Life in a Tube

The most commonly studied bacterium, Escherichia coli (E. coli), has spent most of its recent evolution inside the human gut. Acclimated to that environment, E. coli grows best at 37°C — dividing about every 20 minutes in good conditions. If a researcher inoculates just a few E. coli cells in a rich liquid medium and puts the tube in a shaking incubator, it only takes about a dozen hours to form a population of several billion cells. As these billions of cells continue to divide every 20 minutes, their consumption of nutrients also grows exponentially, eventually exhausting all resources, at which point they enter a kind of dormant state.

E. coli cells are almost completely transparent, but their refractive index differs slightly from the medium in which they are grown. Each cell is only about one micrometer wide, but when millions accumulate in the same test tube, visible light gets scattered, and the liquid becomes opaque.

Compared to animal guts, with their folds, crypts, and periodic floods of bile, a test tube is, from the point of view of a bacterium, a featureless space. Most importantly, it is also the only place on Earth where bacteria don’t have to deal with phages. While we don’t pay much attention to phages, they are everywhere, and Earth would be quite different without them. Every day, phages kill 15 to 40 percent of all bacteria in the ocean, keeping microbial ecosystems from spiraling out of balance.

A thriving culture of bacteria, peacefully growing in a test tube, would surely be an appetizing ground for a bacteria-killing phage to replicate, if it could find its way inside. For this reason, microbiologists are extremely vigilant about phage contamination. Merely mentioning phages at lab meetings will draw nervous looks!

Phages get everywhere, are hard to destroy, and tear through experiments. I’ve seen entire labs shut down for days while whole HVAC systems are sterilized. If there is any detectable sign of unwanted phages, then, researchers stop what they’re doing, autoclave every object possible at the highest possible temperature, and wash the rest with the harshest chemicals available. While many bacteriophages are capable of infecting common laboratory strains, they can usually only spread so far.

The most straightforward strategy by which phages spread is by replicating as fast as they can, infecting as many cells as possible, and killing them in the process. Phages that employ this strategy are called lytic.

One example is T7, a lytic phage that infects E. coli. When T7 enters a bacterium, it uses the cell’s resources to generate copies of itself. This takes about 17 minutes, at which point the cell contains hundreds of phage particles. The phages then burst out of the cell in an event called lysis, searching for new cells to infect. The speed of this process depends on the population density of the bacteria. In ideal conditions, a phage population can expand by a factor of 10⁵–10⁶ every hour.

For bacteria in a test tube, phage infection means annihilation. Billions of cells can get entirely wiped out in two hours. As the bacteria burst and release their contents in the medium, the liquid becomes entirely transparent again.

While the lytic strategy employed by T7 is superb for proliferation, it doesn’t work well for secretly invading a laboratory. If an entire bacteriological culture suddenly collapses for no reason, even the most absent-minded researcher is apt to notice that their cells have been contaminated.

In fact, being too destructive is also a problem in the wild: if a phage eradicates its host too quickly, there might be no bacteria left to infect, meaning death for the phage as well. For that reason, many phages have adopted a more complex life cycle than that of T7, one known as lysogeny.

Take Phage λ, one of the best-studied lysogenic phages. Whenever it infects a new cell, it uses a genetic circuit to choose between two outcomes: either it goes through the usual lytic cycle, filling the cell with virions until it bursts, or it inserts its genome into the bacterium’s DNA. The integrated form is called a prophage.

The host bacterium then carries the phage genome even as it grows and divides. HIV behaves similarly in humans, but the advantage of doing so is much more obvious in bacteria: with a host that divides every 20 minutes, it can be worthwhile for phages to hitchhike for several generations of bacterial division, giving the host time to proliferate on its behalf.

It is even common for lysogenic phages to confer some benefit on their host, helping the infected bacteria outcompete their uninfected sisters and maximizing the prevalence of the prophage in the population.1 There is an interesting puzzle here: if there were an easy way to improve the fitness of the host bacteria, surely the bacteria would already have found it through normal natural selection. How, then, can a parasite grant an advantage that the host wouldn’t have evolved on its own?

One way is to provide the bacteria with genes helpful in the short-term at the expense of long-term sustainability. For example, phage-provided genes may offer costly solutions to temporary problems, like immunity to other pathogens or resistance to specific stresses in the environment.

When the host bacterium is itself a pathogen, phages can benefit from making bacteria more virulent to their host, often against the interests of the bacteria themselves. Some of the world’s most horrific diseases, like diphtheria, cholera, and botulism, are due to bacteria releasing deadly toxins into their host’s body. However, these toxin genes don’t come from the bacteria — they are often poisoned gifts from lysogenic phages.

So when do these dormant lysogenic phages elect to attack? The trigger is usually some indication that the cell is imperiled, whether by DNA damage, oxidative stress, or antibiotics. Some phages even force their hosts to secrete molecules into the environment so they can coordinate their decisions with phages in other infected cells. At the signal, like rats abandoning a sinking ship, the prophage leaves the chromosome, replicates profusely, and bursts into the environment.

In the context of the lab, this often resembles lytic infection, with most cells bursting and becoming transparent. But then, a small subpopulation of bacteria survives, having integrated the phage into their DNA. The prophage then expresses a protein that blocks further infection by the same phage, creating an immune population of cells that resumes growth as if nothing happened.

So, by using lysogeny, a phage can stay hidden in the chromosome of bacteria for extended periods of time. However, in a research lab environment, this tactic can only succeed if the phage manages to integrate itself into bacteria without the researchers noticing. And this is precisely why Φ80 is so cunning.

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The Intruder

A key feature of Φ80 is that it replicates very slowly. While T7 goes through a full lifecycle in less than 20 minutes, Φ80 takes 90 minutes. This is a more dramatic difference than it seems: growth rate compounds with each generation, meaning that T7 can produce 10¹⁰ new particles in two hours, while Φ80 makes barely a thousand in the same interval.

Moreover, while the mechanism Φ80 uses to choose between lytic replication and chromosomal integration has not been fully deciphered, it appears to favor integration far more often than comparable lysogenic phages. As a result, a new infection by Φ80 will not cause the bacterial culture to suddenly collapse and become transparent. Instead, the phage will slowly establish itself inside the population in a way that is invisible to human overseers.

Additionally, it takes very little for Φ80 to switch back into lysis mode. Whereas many prophages use DNA damage as a signal that the bacterium is about to die and it’s time to look for a new host, Φ80 is so sensitive that even the slightest hiccup in DNA polymerization (something that happens routinely when a cell replicates) can make it go lytic. As cells carrying the Φ80 prophage grow, a tiny fraction will constantly pour new phage particles into the medium. As a result, billions of these phages will have accumulated in the tube over a cycle of growth, even though the culture continues to look perfectly healthy to the naked eye.

What’s worse is that this phage is mostly active at temperatures below 37°C. But, 37°C being the standard temperature for E. coli, pretty much every measurement is done at it. A researcher could put the culture on a slide in a microscope heated to 37°C, and everything would look fine. But as they took the culture through the corridor between the shaker and the microscope, the temperature would drop a little bit, and that’s precisely when a fraction of the culture would burst into a barely-noticeable, steady stream of Φ80 particles. In other words, the phage replicates precisely when researchers are not watching.

Even so, escaping detection is only half of its strategy. Φ80 also has an ingenious mechanism to break free from its tube and travel to new samples by hitchhiking on a classic molecular biology technique, thus turning human researchers into unwitting dispersers.

Scientists as Phage Dispersers

The technique in question is called P1-transduction. It is a widely used method for copying and pasting genes from one strain of bacteria to another. To understand how it works, we need to meet yet another phage: P1.2

The key to P1’s utility lies in a quirk of phage biology. During their reproductive cycles, phages use the bacteria’s machinery to produce a massive amount of empty capsids, which then house copies of the phage’s genome. This maintains a little army of fresh phage particles ready to go out and infect the next generation of cells.

Occasionally, though, there’s a mistake in the process: a piece of the host bacteria’s genome gets incorporated into a capsid instead of the phage’s genome. While this normally happens only rarely, P1 makes this mistake unusually often, about 0.1 percent of the time.3

As the phage particles are liberated in the medium and infect other bacteria, the random bit of DNA from the original, infected cell ends up injected into a different one.

This recipient cell notices that there’s a piece of linear, double-stranded DNA floating around in the cytoplasm. (E. coli’s chromosome is circular, so the presence of linear DNA is abnormal — it usually means that the chromosome is broken). In response, the bacterium expresses a suite of enzymes that stitch homologous pieces of DNA together based on sequence similarity, hoping to reconstruct a complete, circular chromosome. Thus, if P1 takes a piece of DNA from the first bacterium, then injects it into a second bacterium, the transplanted piece of DNA will often end up incorporated into the recipient’s chromosome, overwriting the native sequence. This process is called transduction.

Transduction gives scientists a clever way to copy and paste genes from one bacterial strain into another. First, the researcher inserts an antibiotic-resistance gene in the chromosome of one bacterium, called the donor strain, next to the gene they want to move.4 Then, they culture this donor bacterium in liquid broth, grow it up, and add a bit of phage P1. The P1 phages infect the donor cells, filling them up with invisible phage particles, including a few that took on a fragment of the donor strain’s DNA.

Next, these phage particles can be used to infect the recipient. At this point, random fragments from the donor DNA will be injected into the recipient and replace the native sequence by recombination. Finally, a researcher spreads the culture over a Petri dish containing the antibiotic from the first step, along with a chemical that inhibits further infection by P1. At this point, only the cells that have received the right region of the donor’s DNA — the bit containing an antibiotic resistance gene — can survive. And so, overnight, the few cells that received the desired edit will grow to form visible colonies.

When a two milliliter culture of bacteria gets infected by P1, this quickly generates tens of billions of phage particles. 0.1 percent of them will have incorporated a piece of the host DNA by mistake, which means our tube will contain around ten million such mistakes. Each of these pieces of DNA is about 90,000 base pairs long (like the phage’s genome). So, the total amount of donor DNA (mis)incorporated by the phage population will be almost a trillion nucleotides. For comparison, the full genome of E. coli is only 5 million base pairs. Therefore, the phages in our tubes collectively contain the entire genome of the donor bacterium: in fact, hundreds of thousands of copies of it. Add this to a recipient culture with several billion cells, and it’s almost guaranteed that one of them will receive the desired segment and incorporate it in the right place.

This is what makes P1 transduction a quintessential tool for microbiology. Although it relies on a series of unlikely coincidences, the sheer number of particles that fit in a droplet of liquid means it somehow works out in the end. And as long as a genetic element has an antibiotic-resistance marker next to it, it can be easily moved from strain to strain. The most famous application of this is the Keio collection, a holding of thousands of E. coli strains, each with a different gene replaced with an antibiotic resistance marker.

This ease of use made P1-transduction a hugely popular technique, used daily by thousands of biologists around the globe. Unfortunately, its popularity also makes it a perfect conduit for a stealthy parasite like Φ80 to travel from strain to strain. This is because, by a twist of fate, Φ80 has figured out a way to “tag along” with P1 phages.

Consider a routine P1-transduction experiment, aimed at moving a gene from donor to recipient. The donor strain, unknown to the researcher, harbors the Φ80 prophage. When P1 is added to the culture, the population collapses after a few hours; the expected sign of successful phage production. But the arrival of P1 is detected by the dormant Φ80 prophages, which now replicate alongside P1 in massive quantities. The oblivious researcher infects the recipient strain with this mixed phage solution, selects for the antibiotic resistance marker, and sequences the target locus. Everything appears to have worked as expected (the desired gene has been successfully transferred), but the new strain now carries Φ80.

This is, in fact, how Φ80 was discovered in the first place. In the late 2000s, researchers at the University of Illinois in Urbana-Champaign were trying to understand how bacteria repaired their DNA after damage from UV light. They suspected that LigB, a ligase that ties strands of DNA together, might play a role.

To test this hypothesis, the researchers did a classic knock-out experiment: they used P1-transduction to remove the ligB gene, then put cultures of the original bacteria and the modified ones side by side and exposed them to UV light. After exposure, the cultures of the strain lacking LigB mostly collapsed, while the natural strain didn’t. From that, they drew the logical conclusion that LigB must somehow repair UV damage. And yet, their assumptions were all wrong; the LigB ligase has nothing to do with UV damage.

What really happened was that their donor strain was infected with Φ80, which took advantage of the P1-transduction to jump to the new strain. When this strain was exposed to UV light, the DNA damage induced Φ80’s lytic cycle, which looked exactly as if the cells were dying from the damage itself.

But why does P1 activate Φ80? Is it an ancestral relationship evolved over the course of millennia, or is it a new adaptation evolved specifically within the research lab environment? While no one has studied the question in detail, we can find some clues by digging through the scientific archive.

Φ80 was first isolated in 1961 from a collection of clinical samples from Osaka University’s Department of Clinical Evaluation. The version of Φ80 studied by the Urbana-Champaign team is genetically identical to the original, Japanese variety, so any special adaptations must have occurred before 1961. While the phenomenon of P1 transduction was already known at the time, it was not yet used as a method for genome engineering, so it’s unlikely that the “hitchhiking” of molecular biology techniques was a new trait actively selected for.

All in all, it seems likely that Φ80’s ability to infiltrate biology labs is an exaptation: a trait that was originally selected for unrelated reasons, but was later repurposed in a different way after a change of environment. The genetic diversity of phages, after all, is so immense that it is unsurprising that one of them would turn out to be perfectly suited to life in the laboratory.

What Now?

Addressing the Φ80 crisis requires overcoming three obstacles: One is technological, one is social, and one is related to the very nature of biology as a science.

The technological challenge is the most tractable. For a long time, it was only practical to sequence short regions of the genome (using the Sanger method), so researchers would only PCR-amplify and sequence the particular locus they intended to modify. This can grant them great confidence that a strain carries the expected genotype, but it’s basically useless against a phage that inserts itself in a different region of the genome.

While whole-genome sequencing has become much more accessible, it doesn’t really solve the problem. First, it is more expensive than local Sanger sequencing. Second, short-read sequencing (e.g., Illumina) only generates short segments of DNA that must then be assembled on a computer. It is possible to use these short segments to stitch together the entire genome, much like a puzzle, but it’s slightly faster to align it to a reference genome, with the drawback that only sequences that map to the reference are considered. Sadly, the latter method will only detect a hidden phage if a researcher provides the phage genome as one of those references.

In other words, it would be feasible to find Φ80 through whole-genome sequencing, but it would require making two sub-optimal choices: using a slightly more expensive sequencing run and processing the results with a slightly slower algorithm. This is why, in practice, nobody does it. Fortunately, a third generation of sequencing can help: it’s becoming increasingly popular to sequence entire genomes using long-read (e.g., Nanopore) sequencing. This method reads DNA in long segments of thousands of nucleotides, making Φ80’s 46,000 nucleotides of foreign DNA much easier to spot. Hopefully, in the near future, this technique will help us identify Φ80 invasions more readily.

In the meantime, however, it remains difficult to identify Φ80 unless actively looking for it. This brings us to the social obstacles. For a microbiologist to check their strains, they need to be aware of the phage’s existence and dedicate time to checking for it.

Imagine being a fourth-year PhD student who finally managed to measure an interesting, statistically-significant, reproducible difference between two bacterial strains. Their hypothesis makes sense. They did everything right. As far as publication goes, their findings as they are would merit publication. The painful truth is that double-checking for Φ80 contamination is guaranteed to hurt their career. At best, they spend a few hours performing an additional experiment and find nothing; at worst, they discover that their results are artifactual and no longer publishable. There is no reward for discovering that your results are false positives.5

Finally, while Φ80 contamination may be unfortunate, there is something inevitable about this sort of setback given the inherent messiness and complexity of living organisms. So while Occam’s razor is a convenient heuristic, it does not actually work that well for biology; there is always a long tail of insanely complicated speculative possibilities that, every once in a while, turn out to materialize. A stealthy phage spreading from culture to culture? It may not be the most plausible explanation a priori, but it’s plausible enough. And if it’s not Φ80, it could still be any number of improbable but real bottlenecks: autoclave-resistant RNases, traces of phosphorus in the water, novel organelles, or parasites from an entirely unknown domain of life.

This is simply part of life as a biologist. In the 1990s, cognitive scientist Kevin Dunbar spent a year conducting ethnographic observations in a molecular biology lab. According to his notes, 40 to 60 percent of experimental results go against expectation, often for totally unknown reasons. As scientists push the frontier of knowledge, phenomena that were once considered mysterious become settled science, opening the way for new experimental techniques that themselves unearth new mysteries.

This actually makes me fairly hopeful about the future of biology. When people started experimenting with E. coli in the 1940s, they didn’t know a single thing about it. Since then, there has been considerable progress, and we now have at least some information about 3803 of its 4747 genes. The more we understand it, the less room there is left for unexpected artifacts creating misleading results and false interpretations, and the easier it becomes to make progress. Many outlandish oddities, higher-order emergent interactions, and bizarre edge cases loom ahead, but the fog is lifting.

In the end, we should embrace experimental artifacts and contamination not as setbacks to our research agenda, but rather as essential parts of the systems we study. Sometimes, as in the case of Φ80, the artifacts may even have a life of their own.

Antoine Vigouroux is a systems biologist. He writes about science and progress at Telescopic Turnip.

Thanks to Jay and Jasmine for feedback.

Cite: Vigouroux A. “How Φ80 Infiltrates Research Labs.” Asimov Press (2026). DOI: 10.62211/75eh-27rw

By Ulkar Aghayeva

From the late 1980s through the early 2000s, a famous debate played out between the evolutionary biologists Stephen Jay Gould and Simon Conway Morris on the nature of the evolutionary process.

Gould viewed evolution as radically contingent: if “the tape of life” were to be rerun, he argued, even small environmental changes would result in widely divergent outcomes. The likelihood that any major biological innovation, such as multicellularity, photosynthesis, or intelligent life, could evolve again would be vanishingly small, since each of these innovations depended on a combination of rare events.1 The crux of Gould’s idea was that “no important and sufficiently specific evolutionary outcomes are robustly replicable.”

Conway Morris agreed that historical contingencies are pervasive in evolution; however, in his view:

…contingency is inevitable, but unremarkable. It need not provoke discussion, because it matters not. There are not an unlimited number of ways of doing something. For all its exuberance, the forms of life are restricted and channeled.2

In other words, if we imagine life forms having emerged as solutions to problems in a global search space, there are only a limited number of good solutions given existing environmental constraints. Biology is beholden to the laws of physics and chemistry, which limit which solutions are feasible, let alone optimal.

This is why, as species evolve under similar selective pressures toward greater fitness, they acquire similar characteristics. Indeed, even though evolution is contingent at a local level (such as a specific protein sequence or the shape of a flower), it is remarkably predictable at a global level (such as the very existence of proteins and flowers across many species).

Convergent evolution reflects, then, a widespread predictability of life’s design solutions. Similar biological forms and functions often emerge independently in unrelated lineages. For example, ice growth-inhibiting antifreeze proteins evolved independently in Arctic and Antarctic fishes. Although arising at opposite ends of the globe, these proteins converged at both the sequence and structural level: at both locations, they contain a repeating tripeptide motif of glycine–alanine (or proline)–threonine, with the last amino acid fused to a sugar. The severe constraint of survival in freezing seawater pushed these phylogenetically distant fishes to evolve similar molecular solutions.

Similarly, C4 photosynthesis has been documented in more than 60 different plant lineages, including maize, sugarcane, and papyrus. This convergent evolution involves not just a single protein, but a complex mixture of biochemical and structural adaptations that together enable a more efficient use of carbon dioxide.

Nowhere does the power of convergent evolution appear so insistently and compellingly, though, as in the structure of viral capsids, the self-assembling protein shells enclosing viral genomes. Though ranging in size from 20 nm to 800 nm, an estimated 70 percent of viral capsids known to date are icosahedral, shaped like tiny soccer balls.3

This convergence of viral capsid forms is not merely a curiosity of nature. By deciphering viral capsid architecture at the molecular level, scientists have found inspiration for designing more efficient drug delivery vehicles and vaccines. Viral capsid-like protein nanocontainers have provided an excellent solution to the design problem of carrying and delivering a variety of biological cargoes.

But why did viruses converge on icosahedral shapes in the first place? To answer this, we must turn to both genetics and structural biology.

Evolutionary Constraints

From a genetic perspective, viruses must be economical with how much space in the genome they allocate to encoding capsid proteins, as well as all the other functional genes required for replication and virulence. James Watson and Francis Crick termed this the principle of genetic economy. Such a constraint favors highly symmetrical capsid morphologies so that the same capsid proteins, or a very small number of them, can be used repeatedly for building the capsid, rather than coding for a large number of unique proteins.

For example, the hepatitis B virus has only four genes in its genome,4 of which one encodes the capsid protein. An icosahedron has 60 different rotational symmetrical operations (more than any other platonic solid), and so a capsid with icosahedral symmetry significantly reduces genetic costs.

Second, from a geometric perspective, an icosahedron comes closest to a sphere than other platonic solids.5 This grants it the largest volume for a given surface area or, equivalently, for a fixed number of capsid coat proteins. With such high geometric efficiency, more genomic material can be packaged into an icosahedral capsid than into any other shape, be it a cube, tetrahedron, or octahedron.6

The volume of a viral capsid is important not only because of the size of the viral genome, but also because nucleic acids carry a self-repulsing negative charge that must be physically contained. These repeating negative charges are distributed along the length of the nucleic acid molecules, and in solution, they are surrounded by positively charged ions like Na⁺ and Mg²⁺ or by more complex molecules like polyamines, which screen the negative charge of the phosphate backbone.

Capsid proteins often display positive charges on their inward-facing surface that bind the genome, thus partially displacing those ions and facilitating capsid assembly and the condensing of the genome inside the protein shell. In viruses with stiff, double-stranded DNA genomes, the bending of the nucleic acid chain imposes an additional internal pressure amounting to many atmospheres.7

Icosahedral capsids are well suited to accommodate these physical constraints because, due to their quasi-spherical shape, they distribute stress more evenly than polyhedra with fewer faces. This becomes especially important when the virus must survive extreme conditions like drying, pH shifts, or mechanical stress.

In addition to its genetic economy and geometric optimality, the icosahedral packaging of viral capsids is also energetically favorable, such that the assembly of many capsids is highly efficient and spontaneous (it even happens in vitro!).8

The Caspar-Klug theory explores this energetic aspect of viral capsid structure. Its inspiration comes from modern architecture, specifically Buckminster Fuller’s geodesic domes. The same principles of structural stability that work for these domes also apply across orders of magnitude of sizes, from molecular to macroscale, and even down to the atomic level.

The story of how this theory came about thus involves not only structural biologists but also architects, artists and chemists.9

The Structural Biology of Viruses

Donald Caspar grew up in Ithaca, New York, in a family of chemists. He first learned about the tobacco mosaic virus (TMV) at the tender age of ten from the renowned crystallographer Isidor Fankuchen, who frequented his family home.

TMV was the first virus ever discovered, in the late 19th century, and its molecular structure was still unknown when Caspar heard about it in the 1930s. However, it was known to plague the leaves of valuable crops, such as tobacco, tomatoes, peppers, causing leaves to curl and the plants, eventually, to die. Understanding its structure, besides being an exciting problem in basic biology, also promised a path toward fighting the virus.

Caspar’s fateful encounter with Dr. Fankuchen decided his professional path — he went on to study TMV and wrote his doctoral dissertation on “The Radial Structure of Tobacco Mosaic Virus,” explaining how this rod-shaped virus had a helical arrangement of capsid proteins along the length of its RNA genome. After completing his doctorate, he moved to the UK in the 1950s to continue his study of viral structures.

Caspar was not the only scientist attempting to solve the structure of TMV. Indeed, many of the greatest thinkers of the time converged at the University of Cambridge because it had the most powerful X-ray sources for crystallographic imaging, crucial for the structural studies of viruses. James Watson was primarily interested in TMV in hopes of solving the structure of RNA.10

Meanwhile, at the University of London, Rosalind Franklin made excellent X-ray diffraction photographs of TMV capsids, albeit without RNA. A fortuitous encounter with these photographs converted another physicist and crystallographer, Aaron Klug, who had just begun his postdoctoral studies in London on a ribonuclease structure but abandoned it in favor of viruses.11

Caspar met Franklin and Klug in 1955, and initially both Caspar and Klug worked independently on different small “spherical” plant viruses, tomato bushy stunt virus (BSV) and turnip yellow mosaic virus (TYMV), respectively. Caspar’s initial analysis revealed a surprising result: the diffraction patterns of the BSV capsid crystals had a non-crystallographic, five-fold symmetry. This pointed to an icosahedral structure, since each of the 12 vertices of an icosahedron is a convergence point of five edges.12

Crick and Watson had previously hypothesized icosahedral symmetry in spherical viruses, but Caspar’s results provided the first experimental evidence for it.13 A little later, Klug and Franklin reported similar results with TYMV. Even though Caspar and Klug worked on similar research projects, their collaboration wouldn’t start until 1958, after Rosalind Franklin’s untimely death.14

The original model of the viral capsid structure suggested by Watson and Crick, in 1956, viewed the capsid as a curved, two-dimensional “surface crystal” (as opposed to the space-filling 3D crystal), closed in on itself and made of identical subunits — capsid proteins. As each subunit was identical, they interacted in the same way, as in true crystals. But such a model only permitted a maximum of exactly 60 subunits, since the icosahedron has 20 triangular faces, and each triangle can be made of three protein molecules.

Advances in electron microscopy of viral capsids, however, particularly the negative staining method,15 revealed that many, if not most, viruses have a more complex structure than could be explained by the Watson-Crick model. They appeared to possess far more than 60 identical subunits per capsid. A new mathematical theory was needed to account for this seeming anomaly. The solution came not from biology, but rather from architecture.

Birth of the Caspar-Klug Theory

John McHale, a London-based avant-garde artist, learned about the structure of the poliovirus (another icosahedral virus Klug studied with his colleague, John Finch) from a newspaper, The Observer. As a member of an art movement that looked for inspiration in science and popular culture (“Independent Group,” a precursor to “pop art”), he had a keen interest in the structures of Buckminster Fuller — by then a renowned, if eccentric, architect.

McHale immediately saw a connection between the icosahedral poliovirus and Fuller’s geodesic domes, hemispherical polyhedra made of rigid triangular elements, which also had icosahedral symmetry. McHale arranged a meeting between Fuller and Klug in July 1959. Despite Fuller’s impenetrable prose, Klug carefully studied his Synergetic Geometry, an unpublished manuscript of what turned into Fuller’s magnum opus. Even with such preparation, their first meeting didn’t result in insights beyond their shared focus on icosahedral symmetry.

In 1960, Caspar and Klug, now separated by the Atlantic, both read a new book by the author Robert W. Marks on Fuller’s work, The Dymaxion World of Buckminster Fuller, and closely studied the structure of geodesic domes. Caspar also met Fuller in person while the latter was serving as a Professor of Poetry at Harvard University in 1962.16

Both Klug and Caspar were particularly interested in the domes’ light yet sturdy structures, consisting of a variable number of hexagons and the mathematically required and invariable 12 pentagons.17 This exact number is required by Euler’s rule to form a closed polyhedron. With only hexagons, the structure won’t close in on itself and will remain flat.

The framework of geodesic domes is made of rigid rods, or struts. Since each of them can be a part of either a hexagon or a pentagon, their connections are not identical due to the different angles between the sides of those two types of polygons. Even so, the interactions between the struts are similar enough across the entire framework to consider them “quasi-equivalent.”

This key concept, introduced by Caspar and Klug, lies at the heart of their theory of viral capsid structures. Like struts in geodesic domes, identical viral capsid subunits could occupy quasi-equivalent local positions, being a part of a hexamer (a ring of six subunits) or of one of the obligatory 12 pentamers (a ring of five). Since the connections between the subunits do not need to be identical, more than 60 subunits per capsid can easily be accommodated, resolving the mystery which Watson and Crick’s model couldn’t explain.

But the Caspar-Klug theory imposed its own constraints on the permissible number of protein subunits in a viral capsid. It introduced a parameter, T, called the triangulation number18: if each face of the icosahedron is divided into triangles (triangulated), then T describes their quantity.19 Since each of these triangles, in turn, can be made up of three capsid proteins, and an icosahedron has 20 faces, the total viral capsid protein numbers thus become “quantized” in multiples of 60 (60T).

The Caspar-Klug theory thus makes a strong prediction: since each triangular face of the icosahedron can accommodate only a certain number of triangles (1, 3, 4, 7…), only certain multiples of 60 are likely to be observed in viral capsids: 60, 180, 240, 420, and so on.20

The pair presented their research in June 1962, at the Cold Spring Harbor Symposium on Basic Mechanisms in Animal Virus Biology, in a now-famous paper titled “Physical Principles in the Construction of Regular Viruses.” In it, they acknowledged that their model of viral capsid structure “was, in fact, inspired by the geometrical principles applied by Buckminster Fuller in the construction of geodesic domes.”21 22 They even included a photo of Fuller’s dome in Montreal, the Biosphère. Besides introducing the principle of quasi-equivalence and the triangulation number, they also coined the term “self-assembly” to describe the spontaneous nature of viral capsid assembly:

Self assembly is a process akin to crystallization and is governed by the laws of statistical mechanics. The protein subunits and the nucleic acid chain spontaneously come together to form a simple virus particle because this is their lowest energy state.23

For several decades, the Caspar-Klug theory faithfully described all the known viral structures. But with the development of higher-resolution imaging techniques like cryo-electron microscopy, exceptions soon appeared to the strict constraints on the virus capsid composition (60T subunits) predicted by the theory. The first detected outliers were the cancer-causing polyoma and papilloma viruses, which have capsids made up of 72 pentamer facets.

It wasn’t until the early 2000s that mathematical biologist Dr. Reidun Twarock, at the University of York in England, started working out an expanded mathematical framework to explain these anomalies, called viral tiling theory. It retains the Caspar-Klug theory as a special case but also accommodates a broader range of viral capsid architectures.

Unlike hexagons, pentagonal faces cannot be evenly divided into equilateral triangles; neither can they tessellate, or tile, a 2D plane without gaps or overlaps. To account for this, Twarock turned to Penrose tilings, which can, in fact, tile a plane with five-fold symmetry but with a combination of several distinct shapes; one instead uses “kites” and “darts,”24 or kites and rhombs, all of which are four-sided. Such tilings are non-periodic (made of non-identical types of shapes) but still produce long-range order, as in quasi-crystals. Kites and rhombs represent different types of biological interactions — within trimers and dimers, respectively.

A beautiful mathematical result obtained by Dr. Twarock and colleagues says that these non-periodic tilings, representing flattened capsid structures, can be mapped onto a particular subset of the so-called Archimedean lattices. These are tilings of the plane with a combination of polygons making up a repeating unit (like kites and darts). One of them is the regular hexagonal lattice, and it corresponds to the classic Caspar-Klug construction.

But there are three more tilings within Archimedean lattices that were previously undescribed in the context of viral capsid structures. They can be represented as tilings where hexagons are separated from each other by different sets of repeating polygons of other shapes — triangles, squares, or a combination of the two. Such tilings serve as much better models of more complex viral capsid structures, previously impossible to explain within the framework of the Caspar-Klug theory.

In larger viruses, the capsid shell often consists of more than one type of protein. Major capsid proteins can form the familiar icosahedral lattice while minor capsid proteins occupy a second set of configurations not captured by the original Caspar-Klug theory. Herpes simplex virus, for example, has a T=16 capsid, in which the major capsid protein forms pentamers and hexamers, while two other capsid protein types form groups of three molecules that sit in quasi-equivalent locations between them.

A Bacillus phage, with the ominous name Basilisk, is another well-studied case of this generalized quasi-equivalence. Even though such a complex capsid geometry comes at high additional genomic and assembly costs, its composition confers new properties, such as altered stability and different mechanisms of genome release within the host cells, potentially increasing their overall fitness.

Icosahedral Structures Beyond Viral Capsids

Even within this expanded repertoire of structures, icosahedral symmetry remains a constant, a remarkable testament to its apparent optimality as an evolutionary solution to efficient viral genome packaging and protection. Viruses across multiple, phylogenetically unrelated, families appear to have repeatedly rediscovered the icosahedral architecture, making it an exemplary case of convergent evolution that Conway Morris extolled and defended against the radical contingency view of Stephen Jay Gould.

The exact sequences of viral capsid proteins may vary widely, consistent with the “local” contingency of the evolutionary process. But even with this divergence, the tertiary and quaternary structures of capsid proteins and capsid structures of myriad viruses are remarkably similar, illustrating the “global” predictability of evolution. This predictability may be particularly defensible in the case of viruses, since they represent life stripped to the essentials of replication and assembly, and evolving under extreme geometric and genomic constraints.

But geometric constraints of this kind — when a sizable cargo needs to be efficiently packaged inside a container — seem to be at work not only in viruses but across a wide range of biological structures, from the molecular to organismal levels. Indeed, icosahedral symmetry has been found in bacterial microcompartments like carboxysomes (CO₂ fixation organelles in cyanobacteria25), nanocompartments like encapsulins (self-assembling protein shells carrying molecular cargoes), lumazine synthase (a giant enzyme complex catalyzing riboflavin synthesis), and some of the unicellular eukaryotes with mineral skeletons like Radiolarians.26

Icosahedral architectures have also inspired countless artificial protein cages and self-assembling protein nanoparticles for drug delivery and vaccine design. Virus-like particles can self-assemble from proteins in cell culture and are completely harmless, since they lack the viral genome itself or carry a greatly modified version of it that eliminates virulent genes. They can be modified to express antigens on the surface of the capsid, mimicking the repetitiveness and geometry of natural host-pathogen interactions. This grants them high immunogenicity by effectively engaging the receptors of the antibody-producing B-cells in the host organism (which respond more strongly to repetitive antigens). Indeed, two recently WHO-approved highly efficient malaria vaccines, RTS,S/AS01 and R21/Matrix-M, are based on virus-like particles.

In drug delivery, both virus-like particles and artificial protein cages of similar design are used to carry therapeutic loads like enzymes, small molecules, or nucleic acids. Thanks to the relative ease of genetic engineering of viruses, it’s possible to generate libraries counting thousands of virus-like particles. These can be mutated or chemically modified on the surface, to ensure target specificity, or on the inside, to hold onto different molecular loads.

Fully de novo computationally designed protein cages can extend beyond what is typical in nature in terms of their stability, porousness, or even programmable disassembly in response to various conditions. Even so, the high symmetry and repetitive near-identical local interactions afforded by the icosahedral symmetry are still strongly favored in these novel engineered protein nanomaterials. Under exacting physical and informational constraints, both evolution and human engineering have converged on the same shape — a strong attractor in the space of biological containers.

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Ulkar Aghayeva is a science writer and a columnist at Asimov Press. She also writes about science history on her blog Measure for Measure and about music history and cognition on The Bass Line.

Cite: Cite: Aghayeva, Ulkar. “Why Are Viral Capsids Icosahedral?” Asimov Press (2026). DOI: 10.62211/24ou-76ew

By David Brzostowicki

In November 1272, on the Island of Hares — home to both a nunnery and the Hungarian king's summer residence — a nobleman was lured to a purported council meeting, only to be murdered. His name was Béla, Duke of Macsó, a province nestled along the Danube in modern-day Serbia. He was in his early to mid-twenties, childless, and, depending on whom you asked, either a stabilizing force in a fractured kingdom or a dangerous threat.

Through his mother, Princess Anna of Hungary, Béla was reputed to be the grandson of King Béla IV and a member of the House of Árpád, the dynasty that had ruled Hungary for three centuries. Through his father, Rostislav, Prince of Halych, he claimed descent from the Rurikids, the royal house of Kievan Rus’, the predecessor to modern Russia. If true, he bridged two of medieval Europe’s most powerful dynasties.

For over a decade, King Béla IV and his heir Stephen V had fought for control of Hungary. After Stephen V won a decisive victory at the Battle of Isaszeg in 1265, forcing his father to cede the eastern half of the kingdom, Duke Béla found himself on the losing side of a civil war.

When King Stephen V died unexpectedly in 1272, his son, Ladislaus IV, was only ten years old. As the oldest male cousin of the child king, Béla stood next in line to the throne, eligible to serve as regent, or even king, if anything happened to Ladislaus IV. He controlled vast estates in southern Hungary and commanded loyalty from powerful allies. To some nobles, he represented order in a kingdom teetering on chaos. To others, including Ladislaus IV’s mother, he was a threat.

Henrik Kőszegi, head of the powerful House of Héder, also had a personal vendetta against Béla. Once Béla’s mentor, the two had fought side by side in Hungary’s civil wars. But at the Battle of Isaszeg, Béla fled the field while Kőszegi was captured. His subsequent years of imprisonment gave Kőszegi ample reason for resentment.

Various chronicles report that after being invited to the council meeting in the nunnery, Béla was ambushed and murdered. One account states that Kőszegi himself was present and accused Béla of treason before cutting him “to pieces” during the ensuing argument. Another states that it was Kőszegi’s mercenaries who “hacked [Béla] to pieces with swords and maces so that his skull split in two.”

Béla’s sisters, both nuns on the island (today known as Margaret Island), were rumored to have recovered and buried his mutilated corpse within the nunnery walls.

There, the body rested quietly until the spring of 1915. Then, during an excavation of the monastery’s sacristy, archaeologists discovered the skeleton of a young man, buried with his head toward the altar, which bore the marks of extraordinary violence. Anthropologist Lajos Bartucz asked to analyze the remains at the Institute of Anthropology at the University of Budapest.

Twenty-three cut marks scored the bones. Far too many for a duel, these were distributed across the skeleton in a pattern that suggested multiple attackers striking from different directions. The wounds indicated that the assault had continued even after the victim fell, with the body further mutilated while on the ground. Bartucz estimated the skeleton belonged to a male between 20 and 25 years old. Based on the body’s location, wounds, and age, he proposed them to be the remains of Duke Béla of Macsó.

But Bartucz never formally published this analysis. Instead, the bones went into a wooden box with a slip of paper reading, “butchered skeleton of Béla,” and were shuffled (skull and long bones separately) between institutions for decades.

In 2018, interest resumed when researchers at the Hungarian Natural History Museum found postcranial bones that had been missing from the skeleton for eighty years, tucked away in the box with Bartucz’s handwritten note. Zsolt Bernert and Ágota Buzár published preliminary findings on the several long bones, fragments of the pelvis, and vertebrae scored with cut marks.

When biological anthropologist Tamás Hajdu saw their report, he realized exactly where the skeleton’s missing skull was: right near his office at the Department of Anthropology at Eötvös Loránd University in Budapest. It had been misidentified in the Aurél Török Collection, the department’s own repository of skeletal remains.1

Hajdu and colleagues reunited the skull with the rest of the remains and launched a full investigation into the individual’s identity and the circumstances of his life and death.

Their conclusions were finally published in October 2025. They not only confirmed that the skeleton was Béla’s but also demonstrated his dual royal lineage and clarified the number of attackers and types of weapons used. Additionally, they suggested that the murder bore the hallmarks of personal grievance, not just political calculation.

Indeed, this study was the first ancient DNA-based identification of a medieval royal, resolving a century-old archaeological question through a convergence of the suite of scientific techniques known as “complex bioarchaeology.” Its toolkit includes skeletal morphology for biological profiles, stable isotope analysis to read the chemistry in bones and teeth revealing geographic origins and diet, radiocarbon dating for temporal placement, ancient DNA sequencing to identify individuals and establish family relationships, and forensic trauma analysis for reconstructing violence.

Taken together, “complex bioarchaeology” performs a kind of data resurrection, able to bring back individuals like Béla about whom records disagree, as well as those who didn’t merit sufficient attention by chroniclers or, more insidiously, whose recorded lives and deaths were intentionally altered.

The manipulation of historical records is, after all, as old as record keeping itself. Pharaoh Akhenaten’s name was so thoroughly erased after his death that he does not appear in the Abydos King List of Seti I, composed less than a century later. His existence was only rediscovered in the 19th century when archaeologists excavated his abandoned capital at Amarna.

Emperors were likewise erased in ancient Rome. In 211 CE, Caracalla had his co-ruling brother Geta murdered by Praetorian Guards. After executing 20,000 of Geta’s supporters, Caracalla ordered his brother’s name and image excised from every inscription and monument across the empire. Where bronze letters had once spelled out “the Most Noble Caesar Geta” on the Arch of Septimius Severus, Caracalla left text celebrating only himself.

Such erasures and falsifications continue into the modern era. In 1940, Soviet secret police massacred nearly 22,000 Polish citizens in and around the Katyn Forest, then falsified official records to blame Nazi Germany, a lie the Soviet Union maintained until Mikhail Gorbachev acknowledged the truth in 1990.2

While complex bioarchaeology can’t resolve all debates or discrepancies in the historical written record, by unearthing and analyzing physical evidence independent of records, it can help researchers compare what’s written with biological data, and even recover the lives of ordinary people who never merited a chronicler’s attention in the first place.

Duke Béla’s case offered a rare chance to set written records against physical evidence. He was royal, so his murder was chronicled. And his body was preserved and recently rediscovered, so it could be analyzed. What follows is the story of how researchers solved a 750-year-old murder.

Biological Anthropology

To begin their investigation, the team needed to answer a basic question: did this skeleton match details already known about Duke Béla? Historical records indicated he was a young man, probably in his early twenties, from a privileged Hungarian family.

First, then, they needed to determine whether this skeleton belonged to a young man. Estimating a skeleton’s sex relies on multiple features that show statistical tendencies rather than absolutes; even so, the pelvis can be a strong indicator. In females, to aid in childbirth, the pelvic inlet, the circular opening in the upper area of the pelvis, is wider. And the pubic angle, the upside-down V-shape or arch at the very bottom of the pelvis, is broader. In contrast, males have narrower, more angular pelvises.

This particular skeleton had the narrower pelvis of a male. The skull likewise bore masculine features: a prominent brow ridge, a more pronounced external occipital protuberance at the back of the head, and heavier bone overall.

To determine age, anthropologists look at growth plates. In younger individuals, bones are still fusing together. The clavicle, for instance, doesn’t fully fuse to its growth plate until a person’s mid-to-late twenties. The pubic symphysis, the area where the two halves of the pelvis meet at the front, changes texture throughout adulthood, becoming rougher and more porous over time. The cranial sutures, those zigzagging seams where the plates of the skull join together, gradually close with age.

The skeleton showed partially fused growth plates, relatively smooth pubic surfaces, and open cranial sutures, all consistent with a young adult male. But the team was more precise than that, noting that the head of the femur and the medial end of the clavicle, areas that finish fusing in the early-to-mid twenties, showed growth had only recently stopped.

Based on the sternal ends of the ribs and the pubic symphysis, they estimated the man’s age at death as twenty-three, give or take a year. If Duke Béla was murdered in November 1272, that would place his birth around 1249 or 1250 — consistent with extant historical records, which note only that he was born sometime between 1243 and 1252.

There were also things the skeleton didn’t show, the absence of which helped identify its possessor’s place on the social hierarchy. For example, the spines of agricultural workers develop degenerative changes from decades of bending and lifting. Soldiers and manual laborers build up extra bone at the attachment sites of heavily used muscles, showing what are called “entheseal” changes, where repetitive stress creates tiny ruptures that heal and accumulate over time.

But this skeleton showed no such markers, its vertebrae lacking the osteophytes (bony projections) that would have appeared as a result of chronic spinal stress. The muscle attachment sites looked normal, without “facet hypertrophy” (enlarged bony growths on the facets, the small joints connecting the vertebrae). These develop in someone who has spent their life hauling goods or wielding weapons. Whoever this young man had been, he hadn’t worked like a medieval peasant, a common soldier, or a person of the lower classes.

To round out the profile, they had to estimate the skeleton’s height. The long bones, including the femur, tibia, and humerus, were measured and plugged into population-specific regression formulas to build a picture of the whole body. Because body shapes vary around the world, scientists use a formula derived specifically from that individual’s ancestral group, which accounts for differences in build and bone density.

The team calculated that this individual stood roughly 178 centimeters tall, or about five feet ten inches. For 13th-century Hungary, this was above average, consistent with the better nutrition that noble families enjoyed: consistent with an individual like Béla.

The teeth provided the final morphological clue.

“People in medieval times didn’t really care about [dental health],” says Anna Szécsényi-Nagy, PhD, an archeogeneticist at the Institute of Archaeogenomics in Budapest and co-author of the study. “There were big chunks of plaque that we could analyze.”

Microscopic analysis of plaque deposits in the skull’s remaining teeth revealed starch granules from cereals — wheat, barley, and the bread that formed the basis of medieval European diets.3 The samples also showed traces of cooked foods, plant material that had been processed and prepared rather than eaten raw. Peasants wouldn’t have eaten this lavishly.

So far, everything fit Béla’s profile. The skeleton belonged to a young male who had grown up in the right region and hadn’t experienced the physical stresses of the peasantry. But consistency is not proof. Many young aristocrats lived in 13th-century Hungary, and any of them might match this profile. To narrow the identification further, the team needed to establish when this person died and what this person ate (with even further specificity), which can be done through radiocarbon dating.

Radiocarbon Dating

Carbon exists in several forms. Most is carbon-12, which is stable. But a tiny fraction, about one atom in a trillion, is carbon-14, which is radioactive. It’s constantly created in the upper atmosphere when cosmic rays strike nitrogen atoms, and it filters down into all living things on our planet. Plants absorb it during photosynthesis, and when animals eat these plants, carbon is taken up by their tissues.

When something dies, it stops absorbing new carbon. And because carbon-14 is unstable, it slowly decays into nitrogen-14, with half of it disappearing every 5,730 years. It is this principle that underlies radiocarbon dating; when an organism dies, its carbon-14 decays and is not replaced. Less carbon-14 means more time has passed.

This technique emerged from nuclear physics research. Carbon-14 was discovered in 1940, by researchers at the University of California Radiation Laboratory in Berkeley, California. The isotope was first a simple curiosity, but Willard Libby, working at the University of Chicago’s Institute for Nuclear Studies (founded to retain Manhattan Project scientists), recognized how it could be used to date samples.

Libby published his first radiocarbon dates in 1949, including the famous “curve of knowns” — a validation plot showing that the method accurately dated Egyptian artifacts, sequoia tree rings, and other samples of known age. The impact was immediate. By 1960, when Libby won the Nobel Prize in Chemistry, more than 20 radiocarbon dating laboratories had been established worldwide.4

For the first time, researchers could date ancient remains without relying on written records. Yet despite giving archaeologists a universal clock that could place sites on different continents on a common timeline, radiocarbon dating is not perfect. It assumes atmospheric carbon-14 levels remain stable across millennia, which hasn’t always been the case.

An example of such a fluctuation can be found in a study conducted by the Groningen radiocarbon laboratory in the Netherlands, in which tomatoes bought fresh from the market at the time of the study appeared to be 1,300 years old.

So what happened? These tomatoes had been grown in greenhouses where the air was enriched with carbon dioxide (CO₂) to boost plant growth. The CO₂ came from burning fossil fuels like coal, oil, and natural gas, all of which are millions of years old and had started decaying long ago. The tomatoes absorbed this “dead” carbon instead of normal atmospheric carbon, making them appear far older than they actually were.

Something similar happened when researchers tried to date Duke Béla’s skeleton. The team turned to István Major, a radiocarbon specialist at Hungary’s Institute for Nuclear Research in Debrecen, which houses one of Central Europe’s leading accelerator mass spectrometry facilities. His laboratory has spent decades refining techniques for dating difficult samples such as cremated bones, contaminated materials, specimens that confound standard methods.

Béla’s skeleton brought back dates too early, clustering around 1030-1230 AD. At that time, “the nunnery couldn’t have even been established and built,” says Szécsényi-Nagy. “It was totally impossible.” (Indeed, the monastery hadn’t been founded until 1259).

At first, contamination was suspected. The skull had been treated with glue, paper, and plaster during earlier conservation efforts, and these materials might have introduced foreign carbon. The team tried multiple approaches: sampling different bones, separating inner and outer layers of bone, and using aggressive chemicals to thoroughly clean out contaminants. Despite all this, the results kept showing the burial took place long before Béla’s time.

A resolution finally came from a different type of analysis. In addition to carbon-14, bones contain other forms of carbon and nitrogen that don’t decay. The ratios of these stable isotopes can reveal information about diet. A high ratio of nitrogen-15 to nitrogen-14, for instance, indicates a diet rich in animal protein, like meat, dairy, or fish.

Upon checking Béla’s stable isotopes, “We figured out that he had a high-protein diet, so he ate a lot of meat,” says Szécsényi-Nagy. “And it is very probable, living or spending most of his time close to the Danube [river], that he ate lots of fish.” Béla’s nitrogen values were elevated well above the range typical for people eating mostly plants and land animals.

As it would turn out, freshwater fish pose the same problem as greenhouse tomatoes (only for a slightly different reason). Rivers like the Danube flow over ancient limestone bedrock, dissolving carbon that’s been locked in the rock for millions of years. Fish absorb this old carbon as they feed, and it accumulates in their bodies. When a person eats those fish, the old carbon gets incorporated into their bones. This is called the “freshwater reservoir effect,” and it was readily apparent in Béla’s bones: they contained less carbon-14 than they should have because he’d been eating carbon that was already “ancient” when he consumed it, thus distorting the dating results.5

Once Major’s team understood the confounder, they could model what the dates would look like if they corrected for it — testing shifts of 50 to 200 years to account for old carbon in Danube fish. The corrected dates aligned with the late 13th century.6

Additionally, they analyzed the mineral fraction of the bone rather than the collagen, the latter of which would lock in the older carbon. Bone mineral incorporates carbon not just from food but also from inhaled carbon dioxide and blood bicarbonate — sources that aren’t affected by the freshwater reservoir effect. The mineral carbonate dates clustered around 1170-1260 AD, consistent with a death in the late 13th century (and with historical chronicles that place Béla’s murder specifically in November 1272).

By this point, the investigation had answered some fundamental questions. Strontium isotopes placed the remains of this person’s childhood in the Hungarian basin, and radiocarbon dating put their death in the late 13th century. Each line of evidence had narrowed the possibilities, but further identification required ancient DNA analysis.

Ancient DNA

For most of history, forensic anthropology was a descriptive science. Researchers could establish a biological profile — sex, age, stature, ancestry, evidence of trauma — to narrow the pool of possible identities, excluding candidates who didn’t match. But positive identification required comparing remains against records created during the person’s lifetime: dental charts, medical X-rays, documented injuries. Without such records, identifying a dead person was infeasible.

The first major breakthrough came in 1984, when British geneticist Alec Jeffreys developed DNA fingerprinting at the University of Leicester. By exploiting regions of the genome that vary dramatically between individuals, he could produce a banding pattern unique to each person. The technique revolutionized criminal forensics and paternity testing, but it required relatively intact genetic material.

That posed a problem for ancient remains. DNA survives in bone far longer than in soft tissue because it becomes entombed within hydroxyapatite, the dense crystalline mineral that gives bone its rigidity. But it still degrades through purely chemical processes, shattering into fragments too short for traditional fingerprinting to read.

A way past this bottleneck came in 2005, when 454 Life Sciences released the first commercial next-generation sequencer. Well-suited to ancient DNA analysis, next-generation sequencing (NGS) permits the reading of millions of DNA fragments simultaneously rather than one at a time, using software to align the overlapping pieces against a reference genome.

NGS was vital in cracking open Béla’s identity. But before they could sequence his genome, they had to extract the degraded fragments and build sequencing libraries from molecules that had been disintegrating since the 13th century.

At the Institute of Archaeogenomics in Budapest, Szécsényi-Nagy and Noémi Borbély began their ancient DNA analysis by drilling into the petrous bone on the skull. The petrous bone ossifies early in fetal development and undergoes almost no remodeling throughout life, creating a stable mineral matrix where DNA remains entombed.

They then followed the Dabney protocol, a standard method for ancient DNA extraction developed in 2013. The protocol calls for dissolving 50 milligrams of bone powder in a chemical solution overnight so the calcium phosphate matrix is broken down, releasing the DNA. Meanwhile, enzymes in the solution digest proteins and other contaminants. By morning, the powder becomes a murky liquid containing ancient DNA mixed with bacterial and fungal sequences.

Extraction takes two days: the first to dissolve the bone and release its DNA, and the second to purify it, followed by an additional two of “library preparation,” which involves attaching molecular tags so the sequencing machine can read each fragment and trace it back to its source.

The sequencing took three to four weeks, focusing on two critical regions: mitochondrial DNA and Y-chromosome markers. Mitochondrial DNA traces maternal descent. Every human cell contains hundreds of mitochondria, tiny structures that generate cellular energy, each carrying its own small genome. We inherit our mitochondria exclusively from our mother, who inherited hers from her mother, and so on — an unbroken chain of maternal inheritance.

Béla carried haplogroup U3b3 in his mitochondrial DNA, a lineage rooted in the Near East and southeastern Europe. This pointed toward Byzantine ancestry, consistent with the historical record: his maternal grandmother was Maria Laskarina, daughter of a Byzantine emperor.

Y-chromosome DNA traces paternal descent. Unlike other chromosomes, which shuffle their genetic material each generation, the Y chromosome passes from father to son essentially unchanged. Mutations accumulate one at a time, creating a linear record.

Béla belonged to a Y-chromosome lineage shared by the Rurikid dynasty — descendants of Rurik, a ninth-century Varangian prince who established the ruling house of Kievan Rus’. His Y-STR profile matched 24 tested descendants of the Rurikids in modern genealogical databases, and aligned perfectly with the anticipated profile of Rurik himself.

The Y-chromosome analysis was particularly delicate, as any contamination from modern DNA would invalidate the results, so the team ran every step at least twice to confirm authenticity. They also ran the sequencing experiments in both Budapest and at Harvard University.

Harvard’s ancient DNA laboratory had isolated the cochlea itself (the coiled structure of the inner ear), which yields up to 65-fold more endogenous DNA than other skeletal tissue. Whereas the Budapest team focused on mitochondrial DNA and the Y chromosome, the Harvard scientists generated genome-wide data, sequencing across all twenty-two autosomal chromosomes because their aim was population history, not individual identification. But this data sat unused.

Szécsényi-Nagy’s team requested the raw sequencing files from Harvard and, with both datasets in hand, could finally check Y-chromosome markers against the whole-genome data. Crucially, they could also run identity-by-descent analysis to measure Béla’s genetic relatedness to other sequenced medieval royals.

Any two people with a common ancestor inherit stretches of identical DNA from that ancestor. But with each generation, chromosomes reshuffle, breaking those shared stretches into smaller pieces. Siblings share long, continuous blocks of matching sequence. Fourth cousins share only scattered fragments. The math is predictable enough to work backward: measure the total length of identical segments between two individuals, and you can estimate how many generations separate them from their common ancestor.

When the team compared Béla’s genome against previously sequenced medieval royals, the genetic relationships matched the family trees with high precision. Béla of Macsó was indeed a descendant of Béla III, the twelfth-century Hungarian king, separated by exactly the four generations the genealogical records predicted. And in 2023, the final piece fell into place: Dmitry Alexandrovich, a 13th-century Rus’ prince whose genome had been published in a separate study, emerged as a distant relative — confirming the connection to the Rurikid dynasty that Y-chromosome analysis had first suggested three years earlier.

“This whole network of relatedness fitted so nicely together,” Szécsényi-Nagy says. “The genetic evidence didn’t just support the historical record; it was locked into place like pieces of a puzzle.”

Forensic Trauma Analysis

The final unanswered question was the manner of Béla’s death. The chronicles claimed he was murdered. The bones could test that claim, but determining specific types of violence on his skeleton required distinguishing whether its wounds had been inflicted during his lifetime (including what might have been his death wounds) or from the damage accumulated over the seven centuries Béla’s skeleton had spent underground.

Every excavated skeleton shows wear: fractures from soil pressure, breaks from careless excavation, and erosion from groundwater. Bones absorb minerals from surrounding earth, staining brown or yellow depending on soil chemistry. This discoloration helps identify when damage occurred. Ancient healed injuries show bone remodeling around the wound. Fresh breaks from modern handling expose pale, unstained bone. The harder question is whether an unhealed, stained wound represents a killing blow or damage inflicted during burial centuries ago.

The answer lies in collagen. In living bones, this protein provides flexibility. A hard blow breaks the bone cleanly, with smooth fracture lines following the natural grain. Centuries after death, once its collagen has degraded, bone becomes brittle and shatters like dry wood, leaving jagged edges that crumble rather than split. But for roughly a decade after death — the “perimortem period”— bone retains enough collagen to fracture like living tissue. Wounds from this window of time leave distinctive signatures like smooth-edged cuts, clean fractures, and breaks that follow the grain. Wounds inflicted at or near the moment of death show no signs of healing.

Béla’s skeleton displayed twenty-six perimortem injuries with no new bone growth around the wound edges: nine to the skull, seventeen to the body. He died from these wounds, or moments after receiving them.

The shape of each wound also provides clues as to what made it. “Imagine you have a block of soap,” explains Martin Trautmann, a forensic anthropologist who collaborated on the research while at the University of Helsinki, “and you use an ax with quite a thick blade. When this penetrates the block, it will push a lot of material to the sides, just because it’s so broad.” A thick blade crushing into bone leaves small parallel lines along the cut where the outer layer was pushed aside. Forensic scientists call this “feathering.” A thinner blade makes a cleaner cut with minimal disruption to the surrounding surface.

In the 13th-century, Hungary had two distinct blade traditions. Western European longswords, designed for thrusting as well as chopping, were symmetric and double-edged, with a gently curved cross-section. Sabers, which had entered Central Europe with equestrian peoples of the Eurasian steppe, were single-edged and curved, with a thin, wedged-shaped cross-section.

Both weapons left their marks on Béla. The wounds to his head and upper body showed the signatures of a lighter, sharper blade wielded in sweeping arcs, consistent with a saber. The wounds to his legs were heavier, with slight crushing of the bone surface, consistent with a longsword’s chopping stroke.

Two weapons meant at least two attackers. But had there been more?

To find out, Trautmann worked with an articulated laboratory skeleton, the kind used in anatomy classes. He marked each of Béla’s twenty-six wounds in their exact positions on the articulated skeleton, matching their length, angle, and orientation.

Each lesion was analyzed for forensic information through both direct visual inspection and radiologic imaging. Diagnostic marks on the damaged surfaces revealed not just where blows landed, but their direction of origin, the angles of impact, and the probable movements of the weapons and attackers. Trautmann also took similar weapons to the medieval saber and sword profiles used by the attackers and fitted them directly into the bone lesions to find out which type of weapon inflicted each.

By combining all this data about wound location, weapon type, strike direction, and sequence, Trautmann could test scenarios against the physical evidence. In his reconstructive analysis, he put one attacker facing the laboratory skeleton’s front, and two facing from the sides, envisioning different sequences of blows and the defensive postures the living Béla would have adopted.

The pattern that emerged was unambiguous, according to Trautmann. “Béla was confronting a person. This person drew his saber, hit him two to three times on the head and upper body. And then the other two people, probably allies of the saber-wielding attacker, flanked the victim from the left and the right — they kind of cut off his retreat … and then they finished him.”

Historical accounts had offered two versions of Béla’s death: an ambush from behind or a dispute that escalated into violence. Cuts to both forearms showed Béla had raised his arms to protect his head in a defensive reflex, which also meant he hadn’t carried a weapon or shield. The wounds were inflicted mostly on the front of his body, so he faced his killers.

Béla’s wounds are consistent with records that suggest that the motive was a heated dispute with Henrik Kőszegi, still angry by Béla’s betrayal during the Battle of Isaszeg, where Béla fled from the battle while Henrik was captured.

That Henrik had not forgiven this is evidenced by Béla’s facial injuries. “[It] looks like the eyes were gouged out and the nose was cut off,” Trautmann explains. “This kind of facial injury is mentioned in written sources as a punitive act for treason and disloyalty” in medieval Central Europe.

Because the assault continued even after Béla had most likely received a mortal wound, it must have been “a strange mixture of cold and hot blood,” Trautmann concludes. “They were prepared to attack, but when they did, they got carried away.”

What the Dead Reveal

Béla’s case offered a rare combination for bioarchaeologists: a nobleman whose death was chronicled by scribes and whose body was preserved. But complex bioarchaeology is revealing patterns with more complicated remains, even those of mass fatalities.

Consider the Bronze Age battle that ravaged the Tollense Valley over 3,000 years ago, when thousands of warriors clashed at a strategic river crossing in what is now northeastern Germany. Before bioarchaeological analysis of the site, many archaeologists doubted that large-scale organized combat existed in prehistoric Europe — weapons in graves were seen as status symbols, and any violence was assumed to be small-scale raiding between local clans.

However, large-scale excavations of the site demolished this assumption. Excavators recovered over 10,000 bones representing at least 150 individuals, almost all young men killed around 1250 BCE. Isotope and DNA analysis revealed the warriors came from across the continent — southern Europe, Scandinavia, Poland — while a 2024 arrowhead study found weapons characteristic of southern Germany and Moravia. The emerging picture is of coordinated, long-distance military mobilization in a region that would remain illiterate for centuries, leaving no written record of what may have been a common practice.

Complex bioarchaeology can also remedy incomplete or inaccurate records. Greek historians celebrated the Battle of Himera in 480 BCE as a triumph of Hellenic unity against Carthage, mentioning reinforcements from Syracuse and Agrigento but no foreigners. Yet isotope analysis of soldiers buried in mass graves revealed approximately two-thirds grew up outside Sicily, while DNA analysis showed nine warriors had genetic affinities with central Europe, northeastern Europe, the Eurasian steppe, and Armenia. They were possibly mercenaries from as far as the Baltic whose contribution was never recorded by ancient chroniclers.

Criminologists use the term “dark figure” to describe the gap between actual crime and what gets reported. Ancient violence has an enormous dark figure, which even complex bioarchaeology struggles to reconcile. Death tolls require institutional memory that ancient societies rarely built. While ancient states kept records, they tended to count the living, not the dead, capturing snapshots of who existed and what they owned, not who had died.7 While ancient states maintained censuses of the living for taxation and labor, systematic registration of deaths emerged primarily in 19th-century Europe and North America.

Complex bioarchaeology cannot resurrect demographic data that was never collected. It can’t tell us how many people died at Tollense Valley; only that the minimum was 150 (based on recovered bones), with the true figure almost certainly far higher. But it can help fill important gaps, offering confirmatory data for ancient mysteries such as Béla. It could also aid in investigating the far more numerous ordinary deaths that historians have failed to notice.

Each excavation and analysis, then, contributes to a growing body of knowledge about how people lived and died. With every skeleton identified and every wound pattern reconstructed, the dark figure shrinks. And while we may never resolve the enduring questions regarding violence and human nature, at least we can now tackle these questions in an evidence-based way. Written history is a starting point, but records kept in calcium, carbon, collagen, and DNA move us further along.

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David Brzostowicki is a journalist whose writing covers emerging research in biomedical sciences, biotechnology, and healthcare. He is currently a graduate student at Florida Atlantic University’s College of Medicine in Boca Raton, FL, where he studies the molecular mechanisms linking vascular health to metabolic protection, with a focus on circadian pathways and endothelial-to-muscle signaling.

Thanks to Anna Szécsényi-Nagy for her generous interviews and explanations on ancient DNA analysis and the study’s background, and to Martin Trautmann for his expertise in forensic trauma analysis. Header image by Ella Watkins-Dulaney.

Cite: Brzostowicki D. “Dead Reckoning.” Asimov Press (2026). DOI: 10.62211/84jy-26we

This essay will appear in our forthcoming book, “Making the Modern Laboratory,” to be published this summer.

By Spencer Wright

It was a revolutionary idea in the 1830s, and it remains one today — virtually anyone can learn to make their own scientific equipment. With a few dollars’ worth of glass tubing, a flame, and a little practice, you can create all kinds of chemical analysis kits. Because the glass itself is airtight, you can control which chemicals go in, and because it’s clear, you can observe what happens to those chemicals as you manipulate them. If they don’t do what you intend, you can reignite the flame, modify your glass apparatus, and try again.

This insight helped build the modern laboratory: Work wherever you want to, but work in glass, and you’ll reveal life’s most intricate mysteries.

The person who catalyzed this idea, Justus Liebig, had the superlative career title of “Extraordinary Professor of Chemistry” (although his job’s “extraordinary” nature may have had more to do with its nominal compensation than anything else). In fact, Liebig wasn’t excited about the position he held, writing to his parents that he had “no great desire” for it. He would have preferred to stay in Paris — the center of the chemistry universe at the time, and a city where, even at twenty-one years old, Liebig had already begun to make a name for himself. But the University of Giessen had offered him a modest stipend to establish a lab, so, in 1821, Liebig accepted the constraints of small-town life and packed himself off there.

The move (and modest budget) forced Liebig to perform chemical analysis in new ways. While in Paris, studying under the esteemed French chemist Joseph-Louis Gay-Lussac, Liebig had analyzed silver fulminate, letting it combust and then collecting the carbon dioxide that resulted. Because carbon dioxide is hard to weigh,1 Liebig had been taught to measure its volume using an eudiometer, a type of inverted, graduated cylinder where gases could be trapped and their volume read from markings on the glass. This device was costly to make and finicky to use, and Gay-Lussac relied on specialized glassblowers to help design, produce, and maintain it. With such infrastructure missing in Giessen, Liebig’s research stalled.

If necessity is the mother of all invention, then ambition is its accelerant. Dissatisfied with teaching pure theory at the University, Liebig founded an independent institute to impart the tactile skills of applied chemistry. And dissatisfied with the equipment available in Giessen, Liebig traveled back to Paris to learn glassblowing — a skill he then passed on to his students.

Even as he gained these practical skills, he picked intellectual fights with prominent chemists in Paris and Berlin, insisting that their methods of analyzing organic molecules (which measured carbon and nitrogen together from a single volume of mixed combustion gases) were flawed. By 1830, Liebig knew how to make his own glassware and was now prepared to back up his published claims of superior analytical excellence.

The result was the Kaliapparat, a twisted glass triangle that Liebig used to analyze the composition of morphine.2 The principle behind it was simple: Fill the bottom of the Kaliapparat with potassium hydroxide, then force morphine’s combustion gases through it. As the gases bubbled through the Kaliapparat’s bulbs, any CO₂ present would react with the potassium hydroxide, trapping the carbon but allowing the rest (hydrogen, nitrogen, and oxygen) to pass through. Then, by weighing the Kaliapparat and subtracting its pre-reaction mass, Liebig could determine exactly how much carbon, by mass, had been in the original morphine sample.

As an analytical tool, the Kaliapparat was middling. Liebig’s original goal had been to determine morphine’s nitrogen content, which proved challenging given that the nitrogen passing through the apparatus commingled and reacted with other gases. In fact, historian Catherine Jackson states in her book Molecular World that it was even self-admittedly a failure. “In private, Liebig was even more scathing. As he admitted to Berzelius [a dominant figure in European chemistry and a correspondent], his method of nitrogen determination was ‘tiresome, time-consuming and, in a word, quite unbearable,’ while nitrogen’s side reactions had driven him to ‘despair,’” she writes. However, the Kaliapparat was indeed reliable for measuring carbon — and at a much lower cost than the volumetric-based Parisian equipment of the day. So when he published his results in 1831, Liebig simply de-emphasized the nitrogen analysis performed with it and focused on the glassware itself, christening it “A New Apparatus.”

It would take a few more years, however, for the vessel to gain widespread adoption. In 1833, Liebig slipped instructions on how to make a Kaliapparat into an article he had translated from French to German. In 1834, one of his assistants also demonstrated how to make a Kaliapparat at a chemistry meeting. And, in 1839, Liebig published a textbook on organic analysis that included instructions on the making and use of such glass vessels. According to Jackson, Liebig’s effort to publicize the device — and encourage other chemists to make their own — was “explicitly pedagogical.” Liebig sought “to overturn Parisian chemical orthodoxy … [wanting] chemists everywhere to see and understand, to make and use the Kaliapparat and to prove its worth by widespread replication.”

Finally, Liebig’s efforts paid off, and the 1840s became a golden era of amateur glassblowing. Chemists everywhere took up the torch, replicating Liebig’s Kaliapparat (a stylized version of which would be used in the American Chemical Society logo in the 20th century) and producing designs of their own. Glass vessels evolved, and organic analysis flourished as scientists could finally determine repeatable values for a sample’s carbon content. But most importantly, glassblowing established itself as a need-to-know process for anyone doing serious chemistry.

While Liebig’s proselytizing encouraged chemists to learn glassmaking, it also helped that glass itself was so cheap and easy to make. Glassmaking materials (silica sand, soda ash, and limestone) were readily available. As a result, glassblowing became professionalized. Entire lab glassware catalogs sprang up, many of which contained both prices and instructions on how to make one’s own instruments.

One prominent glass dealer was English chemist and publisher John Joseph Griffin, who in his 1832 book Chemical Reactions promoted the use of tumblers (later known as “Griffin beakers”). As the need for professional lab glassware suppliers emerged, Griffin established a shop in Covent Garden in 1852. By the time he published his 1866 lab equipment catalog, it included an adaptation of the Kaliapparat. For one shilling and sixpence, a chemist could purchase “Liebig’s Potash Apparatus,” complete with furnace, combustion tube, desiccant chamber, Kaliapparat, and vulcanized caoutchouc (rubber) connectors. For two shillings and sixpence, a specially modified Kaliapparat, made by professional glassblower Heinrich Geissler, was also available.

This modified device, just one of many similar tools that Geissler invented in the latter half of the 19th century, was designed such that it could be set upright on a tabletop. (Liebig’s triangular design, intended to be suspended from a scale, would simply fall over if set on a surface.) Beyond its basic geometry, Geissler made refinements to increase the Kaliapparat’s accuracy, adding integrated desiccant tubes as well as embedding little glass discs within its three glass bulbs, which forced the combustion fumes to bubble more vigorously (and therefore react more fully) as they passed through the potassium hydroxide.

Geissler’s Kaliapparat is especially striking considering how difficult it would have been to fashion in 1866. At the time, a glassblower’s flame was not made by compressed propane and oxygen, as they are today, but by simply blowing air over an alcohol or oil lamp — or, in some cases, over a charcoal fire. “You were either using your breath or a foot bellows,” choreographing hands, mouth, and feet to generate temperatures in excess of 700°C, says Tracy Drier, a master glassblower at the University of Wisconsin. Today’s glassblowers work with oxy-propane torches that render such contortions obsolete, a convenience Liebig and Geissler could not have imagined.

Liebig and Geissler would have also been struck by the material properties of Tracy’s glass, as the glass formulations of their day left much to be desired. Both soda-lime formulations and leaded glass were vulnerable to attack by water and acids, and would become pitted and cloudy after repeated use. They also needed to be carefully handled and were sensitive to sharp changes in temperature. Even Bohemian potash glass, known for being colorless and fairly workable, contained impurities (iron contamination could introduce a faint greenish tinge) as well as bubbles, seeds, and striations (thin waviness from incomplete melting and mixing).

Perhaps unsurprisingly, the features of glass that late-19th-century scientists desperately wanted to improve upon were its optical qualities. This was especially true for those working in the burgeoning laboratory sciences that relied heavily on microscopes. And the key to better microscopes was better lenses — a technology which was being developed primarily in Jena, a town just 250 kilometers west of Giessen.

One of the major challenges lenses contend with is light dispersion. When light passes through glass, different frequencies bend by different amounts (the same phenomenon that creates rainbows in prisms). Dispersion is not an issue for lab glassware. A chemist wouldn’t care much if their Kaliapparat were to create little rainbows on their workbench. But in the nineteenth century, developments in the glass industry tended to come from optics (a big market) rather than beakers (a relatively small one). In a microscope or telescope, dispersion results in blurry, unfocused images as the light’s constituent parts fail to converge at a single focal point.

It was the chemist Otto Schott who took up the creation of low-dispersion glass. Schott grew up in the glass factory his father managed and later studied the chemistry of glass at the University of Jena. When he completed his degree in 1875, he returned home to Witten, where he kept working on glass formulations, and in 1879, managed to melt a batch with especially high lithium content. Confident that he had found a low-dispersion formulation, he sent a sample to Ernst Abbe, a professor at Jena who had been advocating for a systematic study of glass’s optical qualities.

Taken by the young Schott’s enthusiasm, Abbe invited Schott back to Jena to join him and microscope-maker Carl Zeiss in forming the Glass Technology Research Station. The collaboration, credited as “one of the greatest and most productive associations in the history of glass composition,” proved immensely fruitful. Before he had even moved to Jena, Schott succeeded in producing what he called “borate glass,” which contained high amounts of boric acid. Abbe, measuring the optical properties of this sample, wrote Schott to say that the new sample had “solved completely” the issues caused by dispersion.

If the features of soda-lime glass are remarkable, then those of Schott’s borate glass — later known as borosilicate — were simply fantastic. In addition to its low dispersion, the borosilicates he developed in the 1880s were harder, more thermally stable, and more resistant to corrosion than soda-lime glasses. Each of these properties led to better lens performance. Increased hardness meant that borosilicates could be ground and polished more precisely, resulting in denser surfaces that reduced scattering. Borosilicate’s thermal stability — its tendency not to swell much when heated — meant that fewer internal stresses were created during the grinding and polishing process, resulting in a more homogeneous refractive index. And its excellent environmental stability meant that it didn’t corrode when exposed to air, water, and other chemicals (a problem rare in today’s glass, but painfully evident in antique glassware).

Borosilicate is also much more elastic than soda-lime glass, resulting in lenses (and later lab glassware) that could withstand whatever bumps and jostles they would inevitably experience in the laboratory. Schott, Ernst Abbe, and Carl Zeiss would go on to develop dozens of varieties of optical borosilicate glass; by 1886, they were selling 44 different varieties.

While optical glass has been heralded as “one of the key materials of civilization,” the creation of “utensil glass” would become the real workhorse of the modern laboratory. Schott first produced it in 1892, noting in his journal that “introduction of a boric acid content of up to 25 percent” resulted in glass that could be “manufactured into objects subject to thermal shocks or required to compensate for large temperature differences through the wall. Such objects are: boiling flasks, beakers, [and] bowls for chemists.”

Incredibly, his new formulation was rejected by the German patent office, which cited his earlier wares as being similarly durable. Schott tried, and failed, to appeal their ruling, but in the end, he found satisfaction through commercial success instead. And the new formulation, introduced to the market in the winter of 1893-1894, became the standard for lab glassware almost immediately. By the first years of the 20th century, Schott was selling not only “boiling flasks, Erlenmeyer flasks and beakers” but also “round-bottomed flasks, measuring flasks, Kjeldahl flasks, retorts, fractional distillation flasks, evaporating dishes, test bottles and tubes.”

Schott’s advancements quickly made Jena the heart of the glassblowing world. In Germany, both “Jena” and “Schott” would become household names, with streets and even sports facilities paying tribute to the venerated glassblower. And their reach was not confined to central Europe: Because lab glassware was classified as an educational product, it was often exempt from U.S. import duties, allowing the established German industry to outcompete the younger American one for more than a decade. Those living in the U.S. in 1910 would likely purchase their Kaliapparats from a German manufacturer.

This changed in the summer of 1914 — the onset of WWI — when the British blockade prevented German-made goods from reaching U.S. shores. According to a 1917 Bureau of Standards report, the blockade caused “a very serious shortage of glassware.” With German glass immobilized, however, the market was flooded with new domestic entrants. To promote these brands to American chemists, the Bureau of Standards tested five national lab glassware brands and compared them to Jena and Kavalier, the two German brands that had been most commonplace in the years leading up to WWI. Only one of the American companies, Libbey, predated the invention of borosilicate glass (originally founded in 1818 in Cambridge, Massachusetts, as the New England Glass Company, before relocating to Ohio in 1888 and renaming to Libbey Glass Co).

It was the newest entrant to the market — a Corning, New York brand called “Pyrex” — that performed best of all. Pyrex ware had an “unusually low” coefficient of expansion, and its chemical resistance showed “slight superiority” over all but the Libbey sample. The Corning company, already producing pie pans and casseroles under the Pyrex name, was off to the races. By 1916, they were producing beakers, flasks, and glass tubing, and by 1918, the word “Pyrex” was more common than “borosilicate.” By 1927, use of the word “Pyrex” went on to surpass “Kodak.”

This period was undoubtedly the golden age of glassware. During the 1920s and 1930s, a series of glassware providers established standardized ground fittings, allowing chemists to piece together different glass apparatus without the use of corks and rubber connecting hoses. These acted as a single, standard interface design, letting chemists quickly assemble modular experimental setups. Standard ground fittings quickly gained popularity, and in 1930, they were adopted as “CS 21-36” by the U.S. National Bureau of Standards. By 1938, the Pyrex glassware catalog was 130 pages long. Throughout their product line, all connections were compatible with CS 21-36 Standard Taper fittings.

Such fittings were only one innovation among many aimed at greater precision. Until the 20th century, most glassware (even that based on the same design) wasn’t exactly the same size and volume. While glass molds had existed since the first century to help with consistency, minor variation between vessels remained. This was usually addressed by individual calibration. Each volumetric flask or beaker was filled with distilled water at a controlled temperature — typically 20°C — and the water was carefully weighed on a precision scale. Using the known density of water at that temperature, the glassblower could calculate the true volume and etch the calibration mark at the right spot on that particular piece of glass. This meant that two half-liter flasks might have their calibration lines at slightly different heights, but both would contain precisely 500 mL when filled to their respective marks.

During this “golden age,” however, the development of precision-machined metal molds, combined with Otto Schott’s borosilicate glass, which expanded minimally with temperature changes, meant that glassware could be manufactured to consistent dimensions batch after batch.

Despite the proliferation of standardized glassware and instruments, working chemists were still expected to blow at least some of their own. Even in the early 20th century, this was a required skill for PhD candidates at the University of Wisconsin, and glassblowing classes were common parts of four-year chemistry degrees through the 1950s, when trade schools began offering specialty degrees in the subject. During this time, it was not unheard-of for major biotech companies to outfit (but not staff) their own glass shops, with the expectation that working chemists would produce their own supply. As late as 1957, chemistry textbooks contained instructions on how to work glass with flame.

Today, however, most chemists have given up making their own equipment. And glassblowing, once considered a craft essential to the science of chemistry, has become a subcontracted trade. Even so, the material itself remains centrally important: while plastic has made inroads into the laboratory in the form of sterile, inexpensive components like pipette tips, polystyrene tissue culture flasks, petri dishes, and multi-well plates, glass remains key in optical and high-temperature applications.

Jena, too, remains synonymous with glass, today known as “The City of Science and Light.” While the headquarters of Scott AG moved after WWII to Mainz in West Germany, the company maintains major operations in Jena, producing everything from optical fibers and ceramic glass to the deeply practical glassware championed by Schott, Abbe, and that extraordinary professor of chemistry himself, Justus Liebig.

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Spencer Wright is a writer and ersatz engineer living in Brooklyn, New York. Since 2013, he has written the newsletter Scope of Work, which these days vacillates between technical deep dives and essays about living in New York, rewiring thermostats, and explaining photons to six-year-olds.

Acknowledgements: Thanks to Tracy Drier for granting us an interview, and also to Catherine Jackson, whose book Molecular World provided an incredible overview of Liebig’s work. I also sourced extensively from Jackson’s “The Wonderful Properties of Glass,” Liebig’s Kaliapparat and the Practice of Chemistry in Glass, and Jürgen Steiner’s Otto Schott And The Invention Of Borosilicate Glass. Header image by Ella Watkins-Dulaney.

Cite: Wright, S. “Working in Glass.” Asimov Press (2026). DOI: 10.62211/79pj-25qs

When the Human Genome Project (HGP) released its initial draft sequence in 2001, President Bill Clinton hailed it as “the most wondrous map ever produced by mankind.” After more than ten years of work, an estimated $3 billion in research costs, and a “genome war” with Craig Venter’s private company, Celera Genomics, the project had produced a nearly complete sequence of a human genome.1

UK Prime Minister Tony Blair predicted that this map would yield “a revolution in medical science whose implications far surpass even the discovery of antibiotics.” (Whether this claim turned out to be true is debatable.) A few months later, the two teams — from HGP and Celera — published cover stories in Nature and Science, respectively.

Although the quest to sequence a human genome began in 1990, the techniques it used had already been in development for more than twenty years. And those DNA sequencing methods, in turn, were directly inspired by protein and RNA sequencing research stretching all the way back to the 1940s.

In the twenty years after the draft human genome was first released, the average sequencing cost per genome fell roughly one hundred thousand-fold, ending up just north of $500. In that same period, the cost to sequence a million letters or “megabase” of DNA fell to six tenths of a cent.2 This plummeting price is due largely to technological innovation, including new sequencing chemistries, computational methods for assembling raw reads into finished genomes, and highly efficient commercial sequencing machines.

Out of the many sequencing methods developed over the decades, five are particularly important. These are their histories.

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Sanger Sequencing

Fred Sanger was biology’s great decoder. A British biochemist who spent his entire career at the University of Cambridge, Sanger earned two Nobel Prizes in the same field: first, the 1958 Nobel Prize in Chemistry for creating a method to determine the amino acid sequence of proteins (most famously insulin) and, second, a share of the 1980 Nobel Prize in Chemistry for inventing methods to sequence DNA.

After winning his first Nobel, Sanger turned his gaze to RNA, seeking to become the first person to sequence a full strand. He was beaten by Cornell biochemist Robert Holley, however, who reported the full 77-nucleotide sequence of the alanine transfer RNA molecule in 1965.3

Although many scientists today assume that Sanger was the first to figure out how to sequence DNA, that’s not the case. As with RNA, Sanger was edged out by a Cornell biochemist. This time it was Ray Wu, who, in 1970, published a method to “read” specific sections of two bacterial virus genomes, called λ and bacteriophage 186. Wu’s method was only capable of sequencing “cohesive ends,” short single-stranded sections of these particular phage genomes, and so wasn’t considered a “general” solution to the DNA sequencing problem. In 1974, Wu’s lab refined this technique into the first general sequencing method, but it proved extremely labor-intensive and failed to catch on.

In 1975, Sanger published his own DNA sequencing method alongside laboratory technician Alan Coulson, called the “plus and minus” technique. First, scientists mixed the DNA strand to be sequenced with an enzyme, DNA polymerase, as well as a primer, three normal dNTPs and one radiolabeled dNTP. Radiolabeled nucleotides are incorporated into growing DNA strands just like normal nucleotides, but are tagged with radioactive isotopes, such as phosphorus-32 or sulfur-35, so they can be detected using radiation-measuring equipment.

This reaction would contain only low concentrations of the dNTPs and relied upon brief incubation times, so that DNA synthesis would stall at random positions along the template and yield a population of DNA fragments with varying lengths. These unfinished DNA fragments were then purified and used as templates in four “minus” and four “plus” reactions.

For each minus reaction, the purified DNA fragments were incubated together with three of the four dNTPs, meaning each fragment would be extended by DNA polymerase until the missing nucleotide was needed, at which point synthesis would halt.

Plus reactions worked differently: they used T4 DNA polymerase, an enzyme with strong 3’ to 5’ exonuclease activity, meaning it can chew back the end of a DNA strand. In the presence of only one dNTP, T4 DNA polymerase would degrade each fragment from its 3’ end until it reached a nucleotide complementary to that dNTP, at which point the exonuclease activity would be inhibited. This ensured that all fragments in a given plus reaction ended with the same nucleotide.

Since the eight reactions were run on fragments of random length, the eight plus and minus reactions collectively produced DNA fragments of all possible lengths.4 The fragments in these eight reactions were separated by size (using gel electrophoresis) and then imaged with autoradiography. Gels were dried and then placed against X-ray film, allowing the radioactive DNA fragments to expose the film and appear as dark bands, which a scientist could then painstakingly translate into the DNA sequence. In 1977, Sanger and colleagues sequenced the first full DNA genome using this method: a small bacterial virus with 5,386 nucleotides in its genome, called ɸX174 or “PhiX.”

In 1977, Sanger developed a much simpler sequencing method, called “chain termination,” which is today known simply as Sanger sequencing. This technique took advantage of a different type of special nucleotide called a dideoxyribonucleotide, or ddNTP. ddNTPs lack one of the hydroxyl groups present on a normal dNTP, preventing the chemical reaction necessary to add another nucleotide and terminating DNA elongation.

Sanger sequencing reaction mixtures included purified template DNA, a primer, DNA polymerase, and all four dNTPs. Each reaction also included a radiolabeled ddNTP version of just one of the four nucleotides. Only a small amount of each ddNTP was added, however, to ensure that a fraction of the total DNA fragments produced stopped at each occurrence of that base. As with previous methods, separating fragments via length and performing autoradiography allowed scientists to read the final sequence.

A different sequencing method that chemically cleaved DNA at specific bases, developed by Allan Maxam and Walter Gilbert, was the dominant technology into the 1980s. Radiolabeled DNA samples were incubated in four separate reactions, each of which contained a chemical that cleaved after a different nucleotide — either A/G, G, C, or C/T. By adding the right amount of each chemical, it was possible to produce different fragments chopped off at each individual base. The sequence could then be read using gel electrophoresis and autoradiography. Maxam–Gilbert sequencing was easier than the plus and minus method to run and interpret, but was eventually surpassed by Sanger’s chain termination method, which molecular biologists found both technically preferable and more “elegant” since it mirrored the natural copying of DNA.

While Sanger sequencing was highly accurate and less labor-intensive than its predecessors, it still required the use of radioactive reagents and manual sequence recording. In 1986, Leroy Hood’s lab at Caltech replaced the radiolabeled ddNTPs with fluorescently labeled nucleotides, using fluorophores that emitted different colors of light for each base. They were now able to run the products of all four reactions on the same gel and have a computer read the sequence by detecting the color of each fluorescent signal as fragments passed through a laser beam.

The first commercial Sanger sequencing machine was produced that year by Applied Biosystems (ABS), which Hood had co-founded in 1981. Called the ABI 370A, it retailed for $92,500. Since Sanger never patented his method, other companies were free to develop competing products, and by 1988, there were three Sanger sequencing machines on the market. These were followed by numerous others, including the Perkin-Ellmer 3700, used by Celera and the Human Genome Project, and the ABS 3500 Genetic Analyzer, which is still found in many laboratories today.

454 Pyrosequencing

By the time Sanger sequencing was commercialized, the groundwork for an entirely new sequencing chemistry was already well underway. In 1985, Swedish biochemists Pål Nyren and Arne Lundin published a paper illustrating a procedure that measured the concentration of a molecule, called pyrophosphate (PPi), using an enzymatic cascade that emits light. In early 1986, Nyren realized that the method he’d helped develop could be applied to DNA sequencing, because PPi is naturally produced as a byproduct of DNA synthesis.5

Funding limitations prevented Nyren from dedicating much time to the project at first, but in 1993, he was finally able to publish a proof-of-principle. His technique began by mixing the template DNA with a primer, a single dNTP, and three enzymes: the familiar DNA polymerase plus the light cascade enzymes, ATP sulfurylase and firefly luciferase.6 If the dNTP was incorporated into a strand of DNA, PPi would be produced in the chemical reaction. ATP sulfurylase could then convert the PPi into ATP, which would provide energy for the luciferase enzyme, producing light. Thus, it was possible to determine each base in the sequence by cycling through the dNTPs one at a time until light was detected, and then washing extra nucleotides out between each step. By literally rinsing and repeating, the sequence could be recorded one letter at a time without the use of any gels, which often took hours to run and were difficult to automate.

Nyren’s sequencing method earned the name “pyrosequencing” since it revolved around the production of pyrophosphate. At first, pyrosequencing could sequence only short DNA snippets, with a few nucleotides. In 1996, however, Nyren’s lab demonstrated sequencing of up to 15 bases by using a modified “A” nucleotide to reduce their signal-to-noise ratio.7 In 1998, they increased this to 34 bases by adding another enzyme, called apyrase, to the mix; apyrase degraded unincorporated nucleotides, removing the need for constant wash steps.

The year before, Nyren’s lab had also spun off a company, Pyrosequencing AB, to refine and commercialize the technology. Pyrosequencing was not the firm that would bring the technology to market, however; that distinction went to Connecticut-based 454 Life Sciences, who licensed whole-genome pyrosequencing applications in 2003. 454 made chips which enabled highly efficient, parallelized sequencing reactions and released the GS20 sequencer in 2005 for the price of $500,000. The GS20 worked by attaching each individual DNA template molecule to a bead and copying it many times using polymerase chain reaction (PCR). Each bead was then loaded into a well in a microplate, where sequencing reactions would be carried out. The light from luciferase activation could be detected through the bottom of the wells, enabling sequences to be read.

Pyrosequencing wasn’t developed early enough to be employed by the Human Genome Project or Celera, but it was still the first method other than Sanger sequencing to hit the commercial market, marking the start of “next generation” sequencing methods (NGS). Pyrosequencing worked in real-time, though it struggled to accurately capture regions with several of the same nucleotides in a row. This was because the amount of light didn’t always scale cleanly when pyrophosphate was produced through successive reactions.

In 2006, 454 collaborated with Swedish paleogeneticist Svante Pääbo to sequence the first million base pairs of the Neanderthal genome; the project would be completed four years later, albeit with some help from Illumina sequencing. Illumina and other subsequent NGS technologies rendered pyrosequencing non-competitive, and in 2013, 454 was shut down by Roche, which had acquired it six years earlier. The technology is still used today for some applications, but most importantly, it was the first commercially viable alternative to Sanger sequencing, and the first sequencing method that could be fully automated because it didn’t rely on gels or other tedious steps.

Sequencing by Synthesis

In the mid-1990s, University of Cambridge biochemists David Klenerman and Shankar Balasubramanian were trying to solve a fundamental problem: how to watch a single DNA polymerase molecule at work. Their approach used modified nucleotides, called reversible terminators, tagged with four different colors of fluorescent molecules. If one of these “terminators” was grabbed by the DNA polymerase and incorporated onto the replicating DNA strand, it would block the addition of any other bases until removed using a separate chemical reaction.

Klenerman and Balasubramanian’s great insight was that template DNA could be sequenced by synthesizing a complementary strand of reversible terminators; basically, extending the chain one base at a time and determining the identity of each nucleotide by looking at the color of its fluorophore. In 1998, the pair started a company called Solexa to develop the technology.

Detecting fluorescence from a single DNA molecule proved difficult in practice, however. And so, in 2004, Solexa acquired the IP rights to a method called colony sequencing, developed by French scientists Pascal Mayer and Laurent Farinelli, to solve the detection problem. Colony sequencing affixed DNA fragments to a surface and amplified them over and over, generating “colonies” containing massive numbers of identical DNA strands. By reading the fluorescence from each strand in a colony simultaneously, it became possible to determine the base added at each step with much better accuracy, since random errors in individual strands would be averaged out by the consensus signal.

Now that single-molecule detection was no longer necessary, Solexa was able to develop its signature sequencing chemistry. The process takes place on a chip called a flow cell, which contains a lawn of short DNA sequences affixed to its surface. The template DNA is broken up into small fragments, and adapter sequences, complementary to the DNA on the flow cell’s surface, are added to the ends of each fragment. DNA fragments are then passed over the flow cell, where the adapter sequences bind to spots on the DNA lawn. At this point, primers are added, and an initial round of amplification takes place: the short DNA sequences on the flow cell are extended to create sequences complementary to the bound template DNA fragments, which are then washed away. The sequences present in the fragments of template DNA are now affixed directly to the flow cell.

At this point, each bound sequence exists as a single copy, which produces too faint a signal to detect reliably. Colony sequencing solves this by generating clusters of identical fragments through a process called bridge amplification. The adapter on the free end of each DNA strand will be complementary to some of the original, short sequences on the DNA lawn, and when this binding occurs, the strand bends over to form a bridge shape. Another round of amplification takes place, resulting in two complementary strands each directly affixed to the flow cell. This “bridge amplification” process is repeated over and over to propagate the sequence.

From here, the actual sequencing can begin. Primers and fluorescently-labeled chain terminators are added to the reaction mixture, resulting in the addition of one nucleotide to each strand of DNA on the lawn. A picture is taken of the entire chip, then the chain terminators’ blockers are cleaved to allow addition of the next base. This process proceeds until the reaction is complete, resulting in massively parallelized sequencing. The short reads acquired through this process can be combined via a computational technique called paired end analysis, which links reads by analyzing overlapping sections, to generate the whole sequence.

Solexa’s first product, the Genome Analyzer, launched in 2006 with a retail price of $400,000, and the company was acquired by the American genomics firm Illumina the following year. In 2008, the company published a paper demonstrating their technology’s ability to efficiently sequence whole genomes via short reads. Illumina’s method is commonly known as “sequencing by synthesis.” While the label could technically be applied to other methods, including Sanger’s, which also indirectly assesses sequence by detecting the incorporation of nucleotides complementary to the template strand, it’s most commonly used to refer to Illumina’s chemistry.

Since the release of Solexa’s Genome Analyzer, Illumina has created several new sequencing machines designed to fill different price niches. Illumina’s short reads are highly accurate, and the technique has played a crucial role in reducing average sequencing costs.

Unsurprisingly, Illumina has become by far the most common NGS method, maintaining roughly an 80 percent share over the last few years. This is largely owing to its versatility. Illumina sequencing has been used to create new reference genomes, including the common tomato, but has been especially useful in cases requiring repeated sequencing of short DNA sequences. For example, Illumina machines are routinely used to quantify the activity of genome editors like CRISPR; template DNA will either be edited or unedited, and reading the area around the edit many times provides an accurate quantification of editing percentages. Similarly, large numbers of short reads are useful for sequencing ancient DNA, taken from bones or other remains, since such samples often have degraded stretches. In addition to its role in the Neanderthal Genome Project, Illumina has been used to sequence 10,000-year-old human bodies and to track migration and population turnover in Neolithic Denmark.

PacBio SMRT Sequencing

While Illumina ultimately opted for a method that simultaneously detected massive numbers of DNA strands, others still believed that single-molecule sequencing methods offered a better path forward. Sequencing by synthesis requires repeated amplification, which introduces the possibility of error at each step and biases outputs towards sequences readily amplified by DNA polymerase. Single-molecule techniques were billed as a way to sequence DNA with minimal bias while simultaneously reducing cost.

The first such method was developed in biophysicist Steve Quake’s lab at Caltech and commercialized by Helicos Biosciences, but became unavailable after the company declared bankruptcy, saddled by legal issues and unable to find a market niche. These days, the canonical technique comes from a company called Pacific Biosciences (PacBio). Scientists often refer to single-molecule techniques as “third-generation” DNA sequencing, though they’re often also lumped into the NGS bucket with Illumina.

PacBio was founded in 2004 to develop sequencing methods based on work done in the labs of biophysicist Watt Webb and engineer Harold Craighead, both at Cornell University. The previous year, the two had collaborated to create zero-mode waveguides (ZMWs): small containers just big enough to hold a single DNA polymerase and containing tiny holes at the bottom through which light could be detected. They were able to fix a DNA polymerase to the bottom of a ZMW and detect the incorporation of individual fluorescent “C” nucleotides through the holes, which fed into a microscope capable of detecting light emissions.

In 2009, PacBio published a paper expanding the principle into a full-blown sequencing technique. Once again, each nucleotide was labeled with a different colored fluorophore detectable by the ZMW to determine which base had been incorporated. The fluorophores were attached such that they would be cleaved off during the chemical reaction incorporating the base into the growing DNA strand; they would then diffuse out of the ZMW so that the next fluorophore could be detected. Sequencing took place on a chip with many wells simultaneously — a different type of parallelization where each well detected a single DNA molecule undergoing the same basic chemical reaction.

The next year, PacBio developed a new method to allow multiple sequencing passes on the same DNA molecule. Double stranded DNA templates were ligated to two single stranded adapters, creating what the company called a “SMRTbell template.” Sequencing began at a primer on one of the adaptors and could proceed multiple times per molecule due to circularization, in a process called rolling-circle amplification. This helped reduce PacBio’s error rates significantly.

With its core technology in place, PacBio was ready to go commercial. In 2011, the company released the RS sequencing machine, and has since created multiple new machines containing chips with increased numbers of sequencing wells. PacBio calls the technique single molecule real time (SMRT) sequencing, though it’s colloquially referred to simply as PacBio sequencing. Rather than producing short overlapping reads like Illumina, PacBio generates very long reads; at first these were a few thousand bases, but today they can be well over 10,000.

PacBio’s ability to produce extremely long reads makes it a useful complement to Illumina. Indeed, PacBio machines are better at sequencing “confusing” genomes, such as those with many copies of the same gene, long stretches of repetitive motifs, and “structural variations” like large insertions or deletions, which may not show up in short-read sequences. For instance, PacBio was used to sequence a very difficult bacterium called Clostridium autoethanogenum, which contains repeats, nine copies of a single gene, and insertions from bacterial virus genomes — basically the genomic equivalent of a Thomas Pynchon novel.

Nanopore Sequencing

Nanopore is the most recently commercialized major sequencing method, collectively developed by several groups starting in the 1990s. A nanopore is a protein or lipid with a small hole in its center through which other materials, such as DNA, can pass. The first nanopore used for sequencing was ⍺-hemolysin, a protein toxin from the bacterium Staphylococcus aureus, though other biological and synthetic nanopores have since been tested.

In 1996, David Deamer and Daniel Branton’s labs at UC Santa Cruz and Harvard collaborated on a paper showing that when an electric current runs through a nanopore, passing purine (A and G) and pyrimidine (T and C) DNA bases through the nanopore disrupted the current to different degrees. While the technique couldn’t yet discriminate between all four bases, the general idea for a new single-molecule sequencing method was there.

In 2001, Hagan Bayley’s lab at Texas A&M demonstrated a limited sequencing method based on the observation that correctly and incorrectly paired DNA bases disrupted nanopore current to different extents. They tethered a short piece of DNA with a few unknown bases to the entrance of the nanopore, then added other short DNA strands with different bases at the position corresponding to the unknown base on the tethered strand. By looking at which base produced the disruption corresponding to a perfect match, they could guess the unknown nucleotide.

In order to directly assess DNA strands going through the nanopore, two major problems needed solving. The first was that DNA moved too fast to reliably detect; the second was that individual bases still could not be differentiated, just purines and pyrimidines. In 2005, Bayley (who by then had moved to Oxford) made progress on the first issue, working with scientists at the Scripps Institute to slow the template DNA down by adding short “hairpin” structures that partially blocked off the pore. That year, Bayley co-founded Oxford Nanopore Technologies (ONT) to develop the emerging sequencing method. ONT quickly brought together various technologies, licensing IP from the labs of Bayley, Deamer, Branton, and others.

In 2010, ONT combined two technologies addressing each of the main outstanding problems. The first was an engineered nanopore developed in collaboration with Bayley’s lab that could discriminate between individual DNA bases, solving the resolution issue. The second was a trick to slow the DNA down to detectable speeds, using the familiar DNA polymerase enzyme. Mark Akeson’s lab at UC Santa Cruz had identified a specific polymerase from the bacterial virus ɸ29 that replicated DNA at an ideal speed for detection via nanopore. Template DNA strands were replicated just before entering the nanopore, passing through slowly enough for individual bases’ effect on the electrical current to be detectable and allowing the DNA sequence to be read one base at a time.

By 2012, ONT had unveiled its first sequencing data, and Nanopore sequencing quickly established itself as a quick method for generating long reads without DNA synthesis, albeit with a higher error rate than some earlier methods. (Nanopore reads had an accuracy of about 85-90 percent per base in 2017, compared to over 99 percent for Illumina. Recent improvements, though, have boosted this accuracy to more than 99 percent for most applications.)

ONT released its first commercial product in 2015: a handheld machine called the MinION that retailed for just $1000, a fraction of the price of most sequencers. Subsequent releases include more traditional benchtop sequencers such as the PromethION and GridION.

Conclusion

In its early days, sequencing was a laborious (and literally radioactive) biochemical process. Today, sequencing machines are ubiquitous, safe, and much less labor-intensive. This evolution was enabled not just by advances in biochemistry but insights from biophysics and materials science, as well as manufacturing ingenuity that turned lab sequencing setups into machines ready for shipping to customers.

Ultimately, DNA sequencing technology extends beyond these five techniques, but they represent the most transformative and widely adopted methods of the past fifty years. Together, they have enabled physicians to identify disease-causing variants in patients, allowed researchers to sequence entire microbial communities from ocean water or human guts, and opened windows into deep time by recovering genomes from Neanderthals and early humans.

New sequencing methodologies are still under development, too. In 2025, Roche announced a new single-molecule technique called Sequencing by Expansion, which inserts large engineered molecules called ‘Xpandomers’ between nucleotides for more accurate detection via nanopore. Both new techniques and refinements to existing methods are aimed at further decreasing the cost of sequencing, with some groups looking to read an entire human genome for $100 or less. Ultima Genomics met this target with its UG100 sequencing machine, unveiled in 2022 and shipped in 2024. Element Biosciences’ VITARI system, announced in February and expected to ship in the second half of 2026, achieved the same price point with a smaller device. The $100 price tag advertised by these companies includes only the consumables used by the machine itself, excluding labor, data analysis, and other costs.

Anyone able to approach this target stands to benefit tremendously, given the obvious demand for DNA sequencing. For example, recent years have seen the proliferation of cohort studies focused on clinical analyses of whole-genome sequencing data. These include the Stanford ELITE study, which is focused on identifying genetic determinants of aerobic capacity, and the NIH’s All of Us Research Program, which has sequenced well over 200,000 genomes in order to study genetic diseases.

Innovation in DNA sequencing will surely continue, but these five techniques have already transformed a feat that was impossible just fifty years ago into something that can be done overnight.

Correction: An earlier version of this article incorrectly claimed that Frederick Sanger is the only individual to receive two Nobel Prizes in the same field. We apologize for the error.

Evan DeTurk is an MPhil student at Cambridge in the history of science. He writes about biology and its history on Substack. Previously, Evan researched genome editing at UC Berkeley and earned an A.B. in Molecular Biology from Princeton.

Schematics created by Ella Watkins-Dulaney.

Cite: DeTurk, E. “A Visual Guide to DNA Sequencing.” Asimov Press (2026). DOI: 10.62211/58ew-79yt

This essay will appear in our forthcoming book, “Making the Modern Laboratory,” to be published later this year.

In 1942, at the height of British industrial war mobilization, an unlikely cohort scavenged the nation’s coastline for a precious substance. Among them were researchers, lighthouse keepers, members of the Royal Air Force and the Junior Red Cross, plant collectors from the County Herb Committee, Scouts and Sea Scouts, schoolteachers and students. They were looking for fronds and tufts of seaweed containing agar, a complex polysaccharide that forms the rigid cell walls of certain red algae.

The British weren’t alone in their hunt. Chileans, New Zealanders, and South Africans, among others, were also scrambling to source this strategic substance. A few months after the Pearl Harbor attack, the U.S. War Production Board restricted American civilian use of agar in jellies, desserts, and laxatives so that the military could source a larger supply; it considered agar a “critical war material” alongside copper, nickel, and rubber.1 Only Nazi Germany could rest easy, relying on stocks from its ally Japan, where agar seaweed grew in abundance, shipped through the Indian Ocean by submarine.2

Without agar, countries could not produce vaccines or the “miracle drug” penicillin, especially critical in wartime. In fact, they risked a “breakdown of [the] public health service” that would have had “far-reaching and serious results,” according to Lieutenant-General Ernest Bradfield. Extracted from marine algae and solidified into a jelly-like substrate, agar provides the surface on which scientists grow colonies of microbes for vaccine production and antibiotic testing. “The most important service that agar renders to mankind, in war or in peace, is as a bacteriological culture medium,” wrote oceanographer C.K. Tseng in a 1944 essay titled “A Seaweed Goes to War.”3

Agar was first introduced into the laboratory in 1881. Since then, microbiologists have depended on agar to create strong jellies. When microorganisms are streaked or plated onto this jellied surface and incubated, individual cells multiply into distinct colonies that scientists can easily observe, select, and propagate for further experiments. Many of the most important findings in biological research of the last 150 years or so — including the discovery of the CRISPR/Cas9 gene-editing tool — have been enabled by agar.4 Agarose, a derivative of agar, is also essential in molecular biology techniques like gel electrophoresis, where its porous gel matrix separates DNA fragments by size, enabling researchers to analyze and isolate specific genetic sequences.

Agar is so critical that since WWII, scientists have tried to find alternatives in the event of a supply chain breakdown, especially as recent shortages have caused similar alarm. But while other colloid jellies have emerged, agar remains integral to laboratory protocols because no alternatives can yet compete on performance, cost, and ease of use.

From Sea to Table

Microbiologists have been growing microbes on agar plates for nearly 150 years, but agar’s discovery dates back to a happy accident in a mid-17th-century kitchen. Legend has it that on a cold winter day, a Japanese innkeeper cooked tokoroten soup, a Chinese agar seaweed recipe known in Japan for centuries. After the meal, the innkeeper discarded the leftovers outside and noticed the next morning that the sun had turned the defrosting jelly into a porous mass. Intrigued, the innkeeper was said to have boiled the substance again, reconstituting the jelly. Since this discovery, agar has become a staple in many Japanese desserts, from yokan to anmitsu.

Industrial production of kanten (the Japanese name for agar, which translates as “cold weather” or “frozen sky”) began in Japan in the mid-19th century by natural freeze drying, a technique that simultaneously dehydrates and purifies the agar. Seaweed is first washed and boiled to extract the agar, after which the solution is filtered and placed in boxes or trays at room temperature to congeal. The jelly is then cut into slabs called namaten, which can be further processed into noodle-like strips by pushing the slabs through a press. These noodles are finally spread out in layers onto reed mats and exposed to the sun and freezing temperatures for several weeks to yield purified agar. Although this traditional way of producing kanten is disappearing, even today’s industrial-scale manufacturing of agar relies on repeated cycles of boiling, freezing, and thawing.

Because of its capacity to be freeze-dried and reconstituted, agar is considered a “physical jelly” (that is, a jelly that sets and melts with temperature changes without needing any additives). This property makes dry agar easy to ship and preserve for long periods of time.5

Over the years, agar found its way around the world into many cuisines, including those of China (where it’s called “unicorn vegetable” or “frozen powder”), France (sometimes called gélose), India (called “China grass”), Indonesia (called agar-agar, which translates simply as “jelly”), Mexico (called dulce de agar, or agar sweets), and the Philippines (known as gulaman).

Agar is prized among chefs for its ability to form firm, heat-stable gels at remarkably low concentrations — typically just 0.5-2 percent by weight. Culinary agar is available as powder, flakes, strips, or blocks, and makes up about 90 percent of the global use of agar. Unlike gelatine, which melts at body temperature, agar gels remain solid up to about 185°F (85°C), making it ideal for setting dishes served at room temperature or warmer. It is also flavorless and odorless, vegan and halal, and can create both delicate jellies and firm aspics. Yet, while increasingly employed in kitchens worldwide, agar had not yet entered the laboratory.

Before agar, microbiologists had experimented with other foodstuffs as microbial media. They turned to substances rich in the starches, proteins, sugars, fats, and minerals that organisms need for growth, testing with broths, bread, potatoes, polenta, egg whites, coagulated blood serums, and gelatine. However, none worked particularly well: all were easily broken down by heat and microbial enzymes, and their surface, once colonized, became mushy and unsuitable for isolating microbes.

This was especially vexing to physician and bacteriologist Robert Koch, who, in seeking to culture his bacteria, “bent all his power to attain the desired result by a simple and consistently successful method,” wrote bacteriologist and historian William Bulloch in his 1938 book, The History of Bacteriology. “He attempted to obtain a good medium which was at once sterile, transparent, and solid” and got some results with gelatine.6 But gelatine is easily digested by many microbes and melts at precisely the temperatures at which the disease-causing microbes Koch wanted to study grow best.

The woman who ultimately discovered the superior features of agar as a growth medium and brought it to Koch’s attention was Fanny Angelina Hesse. Her foundational contribution to the nascent field of microbiology is often omitted from textbooks. In other cases, she is unflatteringly referred to as a “German housewife” or as “Frau Hesse,” or dismissed as an unnamed technician.

From Plate to Petri Dish

Fanny Angelina (née Eilshemius, from a Dutch father) grew up in Kearny, New Jersey. During her childhood, her family learned from a Dutch friend or neighbor about agar-agar, a common ingredient in jelly desserts in Java (Indonesia), then a Dutch colony. Her mother and, later, Fanny Angelina herself, began to cook with it.

In 1874, Fanny Angelina married physician and bacteriologist Walther Hesse, an investigator of air quality and, specifically, air-borne microbes. In the Winter of 1880-81, Hesse became a research student with Koch in Berlin and experienced firsthand the difficulty of growing microbes on gelatine and the other growth media used at the time.

While raising three children and taking care of the household, Fanny Angelina Hesse supported, documented, and archived her husband’s work, creating stunning scientific illustrations of bacterial and fungal colonies. During the hot Summer of 1881, she watched as Hesse struggled with gelatine-based growth media. Fanny Angelina, recalling the stability of her agar-based desserts, suggested that they try that instead. Hesse wrote a letter to Koch informing him about the switch, and Koch mentioned agar for the first time in his 1882 groundbreaking paper on the discovery of the tuberculosis bacillus.

The change to agar was a marked improvement. The jelly is so effective that it is still an invariable ingredient in what is known today as the “Koch’s plating technique” or the “culture plating method.” As Koch himself noted in 1909: “These new methods proved so helpful…that one could regard them as the keys for the further investigation of microorganisms…Discoveries fell into our laps like ripe fruits.”

Once Koch established the methods to grow pure cultures of bacteria like tuberculosis and anthrax, he demonstrated for the first time that microbes can cause diseases, a feat that earned him the 1905 Nobel Prize in Physiology or Medicine.

However, Koch never credited the Hesses for their discovery of bacteriological agar, perhaps because, at the time, he failed to recognize its importance. Even after he received the insight about agar from the Hesses, Koch stuck with gelatine for years. In 1883-84, during his first medical expedition to Egypt and India to investigate cholera, he tried and failed to grow the cholera bacterium on gelatine media in the hot climate of Cairo (despite using a half-open fridge for incubation), only succeeding in the colder winter of Calcutta.

It is difficult to know exactly when the shift from gelatine to agar occurred. As often happens for scientific breakthroughs, agar was likely adopted incrementally alongside the use of other growth media. In 1913, for example, the first diagnosis of Serratia marcescens as a human pathogen was made by growing it on agar as well as on potatoes.

Nevertheless, by 1905, a report on the seaweed industries in Japan noted the “very important use [of pure-grade agar] as a culture medium in bacteriological work.” It’s safe to say that, around the turn of the 20th century, agar had moved from an inconspicuous kitchen jelly to an indispensable scientific substance.

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A Strategic Substance

Several properties of agar render it a superior jelly. Agar isn’t broken down by microbial enzymes apart from a few species (including bacteria living in marine and freshwater habitats), and it dissolves well in boiling water, making it easy to sterilize. The jelly doesn’t react with the ingredients of a broth, whose composition can be adjusted to meet the nutritional requirements of different microbes, and sets to a firm gel without the need for refrigeration.

Agar’s low viscosity also makes it easy to pour into Petri dishes, and its transparency permits observation of microbes growing on its surface.7 Also aiding in this is its low syneresis (extrusion of water from the gel), guaranteeing less surface “sweating”: Once a plate is inoculated, bacterial colonies stay in place and do not mix.

The jelly is chemically inert since no additives are needed for gelation. This allows chemicals dissolved in the jelly’s aqueous phase to diffuse well, a prerequisite for testing if certain species or strains are resistant to antibiotics or antifungals. In these simple assays, zones of growth inhibition of bacteria or fungi (or their absence) point to the effectiveness of (or resistance towards) antibiotics or antifungals.

But agar’s superior qualities come with complex chemistry. “To speak of agar as a single substance of certain (if known) chemical structure is probably a mistake,” wrote phycologist Harold Humm in a 1947 article. According to the Food and Agriculture Organization of the United Nations, agar is merely recognized as “a hydrophilic colloid extracted from certain seaweeds of the Rhodophyceae class.” In terms of its actual composition, agar is mostly a combination of two polysaccharides, agaropectin and agarose, which themselves are complex and poorly-characterized polysaccharides made mostly (but not exclusively) from the simple sugar galactose.8

Agar comes from multiple sources, as many red seaweeds are “agarophytes” (that is, seaweeds containing agar in their cell walls). Species of Gelidium are the most important source of bacteriological (lab-grade) agar. Other main agarophytes, largely used for culinary agar, include red seaweeds from the genera Gracilaria, Pterocladia, Ahnfeltia, and others. Species from the genera Eucheuma, Gigartina, and Chondrus have been used as agarophytes in research during agar shortages.9

One striking characteristic of Gelidium is that it must be wild-harvested rather than farmed. Unlike Gracilaria for culinary agar production, Gelidium grows slowly and thrives only in cold, turbulent waters over rocky seabeds, conditions nearly impossible to replicate in aquaculture. This dependence on wild harvesting explains the need for seaweed collectors during WWII, and continues to make Gelidium a strategically critical resource.

While Gelidium seaweeds can be collected by gathering fragments washed ashore, mass production of agar requires steady, large quantities.10 Harvesters in New Zealand during WWII had to “walk beside a boat, waist to armpit deep in water and feel for the weed with their feet.” Handling large volumes of wet seaweed (which yields less than five percent agar) was challenging. Then as now, when Gelidium is harvested by scuba divers from rocky seabeds, collectors have to understand the life cycle of the algae, find the most likely locations for its growth, and prevent overharvesting to safeguard future yields.

Given its auspicious position on the Atlantic coastline, Morocco has been the main source of Gelidium for at least two decades, and demand for bacteriological agar continues to grow. Yearly global consumption increased from 250 tons to 700 tons between 1993 and 2018, and is currently estimated at around 1,200-1,800 tons per year, according to Pelayo Cobos, commercial director of Europe’s largest producer of agar, Roko Agar.

The Future of Agar

Amid such rising demand, it’s understandable that researchers worried when Morocco reduced exports of agarophytes in 2015. This shortage — due to a combination of overharvesting, climate warming, and an economic shift to internal manufacturing in the North African country — not only caused alarm but a three-fold price increase of wholesale bacteriological agar, which reached $35-45 per kilogram. (At the time of writing this in late 2025, factory agar prices are sitting at about $30 per kilogram, according to Cobos.)

A few years later, in 2024, researchers in multiple labs were horrified to notice toxic batches of agar for reasons as yet unclear. After they observed a worrying lack of microbial growth (impeding their ability to carry out basic experiments), they switched to different agar suppliers, and their results improved.

This was not the first time that microbiologists experienced problems with agar. A phenomenon called “The Great Plate Count Anomaly” baffled researchers in the early 20th century when they observed that the number of cells seen under a microscope didn’t match the actual number of colonies growing on an agar plate. Investigating this discrepancy, researchers found agar itself to be the culprit: when nutrient broths are heated with agar during boiling, harmful byproducts (hydroperoxide) can form due to the reaction of agar with phosphate minerals contained in the media. Researchers can avoid this by autoclaving agar separately from the nutrient broth, or by reducing the amount of agar used.

This anomaly is indicative of the larger challenge of culturing various microbial species, referred to as microbial “unculturability.” This cannot be explained by the use of agar alone or by the substitution of an alternative gelling agent, but rather by the difficulties in consistently recreating on an agar plate the multi-variable environment in which microbes grow naturally. Given such challenges, the risk of shortages, and the vulnerabilities of the agar supply chain, why is it so difficult to find suitable alternatives?

It is not for lack of trying. In some cases, microbiologists have ditched the Petri dish altogether, using microfluidics for manipulating and growing cells. However, these approaches aren’t likely to be adopted at scale as they require less common, less practical, and more expensive devices. So, what about other growth media?

By WWII, scientists had already begun looking at alternative gelling substances for routine use in bacteriology, but concluded that agar was still better as it is both firmer and easier to handle. Today, some specialized microbiology applications use the colloid carrageenan (extracted from red seaweed Chondrus crispus, or “Irish Moss”), a more transparent and less auto-fluorescent alternative to agar (agar emits its own background fluorescence when excited by light). However, for routine bacteriological use, carrageenan is more difficult to dissolve, requires higher concentrations, can degrade at high temperatures, and forms weaker gels, which may result in puncturing its surface during the plating of cells.

In some cases, alternative gelling agents might provide faster results. Researchers observed that bacterial cellulose and another bacterial polysaccharide, Eladium, allow a 50 percent increased growth rate for various bacteria and yeasts (as compared to their growth on agar), including higher biomass yields or faster detectable biofilm formation. However, both substances are still not as cheap and readily available as agar.

Guar gum, a plant colloid, costs less than agar and is better suited for growing thermophilic bacteria, but is also more difficult to handle, being more viscous and less transparent. The bacterial polysaccharide xanthan is cheaper as well but forms weaker jellies that, as with carrageenan, might result in puncturing its surface. Other colloids, like alginate (from brown seaweed) and gellan gum (from a bacterium), don’t set solely based on temperature and require additives for gelation. These additives might interfere with microbial growth and make the preparation of those jellies less handy than agar plates.

Thus, despite much effort, no gelling agent has yet been discovered that possesses all the properties and benefits of agar. Agar continues to be the best all-arounder: versatile, cheap, and established. And, if Gelidium agar should ever run out, and another colloid is not at hand, microbiologists could revert to culinary agar, which, although not as pure and transparent, offers a low-cost alternative to lab-grade agar.

It’s also worth noting that even if alternatives superior to agar were found, scientists are reluctant to abandon established protocols (even when microbiologists do use other jellies, they often still add agar to the mix, for example, to increase the gel strength of the solid media). As agar has been the standard gelling agent in microbiology for around 150 years, an enormous infrastructure of standardized methods, reference values, and quality control procedures has emerged around its specific properties. Switching to a different medium (even a superior one) means results may not be directly comparable to decades of published literature or to other laboratories’ findings.

So it is that agar continues to be the jelly of choice in laboratories around the world. As Humm wrote in 1947: “Today, the most important product obtained from seaweeds is agar, a widely-used commodity but one that is not well known to the general public.” Almost 80 years later, it might be better known, but its importance hasn’t dwindled.

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Corrado Nai has a Ph.D. in microbiology and is a science writer with bylines in New Scientist, Smithsonian Magazine, Small Things Considered, Asimov Press, and many more. He is currently writing a graphic novel about Fanny Angelina Hesse and the introduction of agar in the lab called The Dessert that Changed the World, which can be followed and supported on Patreon.

Thanks to Steven Forsythe for sharing a report on the use of agar seaweed in Britain during WWII, Barbara Buchberger at the Robert Koch Institute for pointing out Koch’s use of gelatine for the identification of cholera, and the surviving relative of Fanny Angelina Hesse for sharing a trove of unpublished material.

Cite: Nai, C. “The Origins of Agar.” Asimov Press (2026). DOI: 10.62211/12pq-97ht

By Taylor Rayne

Smell is our most primal and, arguably, most emotionally potent sense. It summons memories, shapes taste, and influences behavior: the aroma of coffee is capable of enhancing alertness well before caffeine ever reaches the bloodstream. A hint of sunscreen collapses decades, taking us back to youth; but, pinch the nose, and suddenly a slice of apple is hard to distinguish from a piece of raw potato.

Despite its significance, scent remains the most mysterious of our senses. Unlike vision or hearing, it resists straightforward formalization. The challenge lies not only in the vast molecular diversity of odorants, which vary in far more ways than photons or frequencies, but also in the effort to build a shared vocabulary and technology capable of codifying subjective sensation. So while machines have learned to see through computer vision and hear through signal processing, scent remains stubbornly analog. There has been no RGB of odor, no Fourier transform for smell.

At least, until now.

Tech giants, including Google, startups such as Osmo, and even traditional fragrance houses like Givaudan have begun turning to AI to probe the possibility of digitizing smell. By encoding scent molecules into 1s and 0s, their hope is to better understand and manipulate this sensory modality. Just as “computer vision” has helped us realize that sight is not just passive image capture but an active process of prediction and interpretation, researchers hope that programming smell will illuminate the many mysteries of olfaction.

Beyond providing further insight into olfactory biology, digital scent could have many practical (and quite profitable) applications, which is why its proponents, from defense agencies such as DARPA to corporate conglomerates like Estée Lauder, have invested in it. Computational smell could, for example, help detect threats and information invisible to cameras, such as gas leaks, food spoilage, disease markers in breath, and even counterfeit products. It could also reduce reliance on resource-intensive natural ingredients used in perfume and other odorants by, for instance, finding chemically synthesized molecules capable of evoking the same brain patterns. And finally, it could lead to the creation of entirely novel smells, revealing a vast, untapped chemical palette that would otherwise be unattainable without the aid of technology.

The Bacterial Beginnings of Smell

Long before life evolved eyes and ears, the world was encountered chemically. This took place as molecules permeated and diffused across cell membranes, performing a metabolic exchange between animate and inanimate matter.

Smell, our most ancient interface with the environment, originated over 3 billion years ago, in bacteria adrift in the primordial ocean. These early organisms navigated chemical gradients in the water, detecting molecules to swim toward food and away from danger. This ability, known as chemosensation, is the most rudimentary form of smell.

Such “sensing” relies on receptor proteins embedded in the cell membrane, acting like molecular locks awaiting the corresponding chemical key. When a passing odor molecule fits into a receptor’s binding site, it changes the receptor’s shape, setting off a cascade of signals inside the cell that direct the organism’s movement.

Over time, these molecules didn’t just guide survival; they encouraged multicellular life. As cells began clustering together, the exchange of semiochemicals — molecular signals that transmit information within and between species — began to influence behavior, enabling aggregation and synchronization, and laying the groundwork for cellular cooperation. Plants, for instance, release green leaf volatiles such as cis-3-hexenal (the familiar scent of freshly cut grass) when attacked, both warning neighboring plants and attracting the animals that prey on herbivores. Human infants, meanwhile, are drawn to the distinctive odor of their mother’s milk, which both stimulates feeding and regulates their earliest physiological rhythms. And among insects, ants are famous for deploying pheromones such as iridodials, which direct entire colonies to forage or fight in concert.

Once the first tetrapods emerged from the sea and embraced life on land, smelling evolved to become ever more refined under newfound terrestrial pressures, including adapting to novel volatile odorants and the more variable conditions of airborne climates. As these early terrestrial vertebrates expanded a chemosensory repertoire that had once been far more limited in their aquatic ancestors, olfactory systems likewise continued to evolve. Over the next hundreds of millions of years, the neural structures supporting our own sense of smell increased in sophistication.

Today, roughly two to five percent of our genetic blueprint concerns itself with smell. While it may seem a small fraction of the whole, it is the largest gene family in the human genome. At any given time, 77 percent of the 356 distinct olfactory receptors are expressed in the lining of the nasal cavity, each tuned to the molecules that make up the world’s myriad smells. The receptors expressed vary between individuals, with only 90 receptors commonly found in all people. Together, this suite of receptors is responsible for every experience of scent we encounter, and the variability between individuals is likely behind smells’ subjectivity.

To understand how this olfactory complexity works, consider the single inhalation that follows biting into a ripe strawberry: the rush of aroma, the sweet, tangy burst blooming in the nose, created not by a single compound but by a volatile molecular cocktail. There is no one single molecule responsible for the smell of strawberry, but rather a family — namely furaneol (caramel-sweet), methyl and ethyl butanoate (fruity), methyl 2-propanoate (fruity), hexanal (green and sharp), and cis-3-hexenol (leafy-fresh) — that evaporate and surge through the nasal cavity.

In each nostril, this medley of molecules dissolves into the mucus layer lining a 2.5 cm² patch of tissue known as the olfactory epithelium. Studded across this small region is a mosaic of roughly 10 million olfactory sensory neurons,1 each expressing only one type of olfactory receptor protein. In one breath, an odorant molecule, be it furaneol, cis-3-hexenol, or any other, activates a unique combination of receptors, similar to striking a subset of keys on a piano. This ensemble of activated neurons forms a distinct pattern that the brain reads as “strawberry.”

Crucially, no two scents ever strike the same pattern. The combinatorial activity of hundreds of receptor genes allows humans to detect and discern more than a trillion distinct odors.

While some olfactory receptors respond broadly, meaning they can recognize and bind to several different structurally-related molecules, other receptors are exquisitely selective and bind to only one specific shape or stereoisomer.2 For instance, the two mirror-twin forms of the organic compound carvone smell strikingly different — one like spearmint (R-carvone), the other like caraway (S-carvone) — underscoring the nuance the nose brings to discriminating between such molecular mirror images.

The resultant signal, whether “caraway,” “spearmint,” or “strawberry,” travels to the olfactory bulb, a bipartite nerve structure nestled at the base of the skull, just above the nasal passages. There, neurons expressing the same receptor type converge on specialized structures called glomeruli, the crucial processing hubs that sharpen and refine sensory input en route to deeper regions of the brain involved in odor discrimination.

Each glomerulus acts as a dedicated module for a single receptor type, receiving input from thousands of olfactory sensory neurons scattered throughout the nasal epithelium, but all tuned to the same molecular features. Within these spherical tangles of neural connections, the incoming signals undergo their first round of processing: they’re amplified, filtered, and integrated by local interneurons that enhance contrast between different odor signals.

Unlike other senses, these olfactory signals take an unusual route through the brain. While vision, hearing, and touch all pass through a brain region called the thalamus before reaching higher brain regions, smell bypasses this checkpoint. Instead, odor information travels directly from the olfactory bulb to the amygdala and hippocampus (two brain structures central to emotion and memory) before reaching conscious processing areas. This anatomical shortcut may explain why smells can trigger vivid memories and strong emotions before we’ve even consciously identified what we’re smelling.

Yet, while the nose has been anatomically mapped, receptors sequenced, and neural pathways charted, predicting a molecule’s scent has remained a mysterious exercise. The question of why certain configurations of matter smell one way and not another persists. In other words, why does a molecule such as furaneol activate the receptor signaling “jammy sweetness”? What makes one molecule smell “grassy” and another “creamy,” one trigger nausea and another nostalgia?

The prevailing hypothesis defines odorant molecules as ligands, specialized binding molecules that fit into olfactory receptors like a lock and key. This interaction activates the receptor, initiating an electrical response in the brain, a unique pattern of activity associated with a particular scent. While molecular structure has long served as a proxy for predicting smell, particularly for researchers and fragrance chemists, the so-called Structure-Odor Relationship (SOR) paradox endures: molecules of nearly identical structure can smell worlds apart, while those with little in common can smell strikingly similar.

Take musks,3 for instance: this family of compounds includes hundreds of molecules with vastly different structures and molecular weights, ranging from small macrocycles to large polycyclic frameworks. Yet, despite this diversity, many share a common warm, powdery, and animalic scent profile that defies straightforward structure-to-smell prediction.

An Industry for Smell

The speculation that chemical structure corresponds to scent dates back millennia, alongside the use of fragrant materials in ceremonial and cultural practice. From the early Greek atomists’ theories of microscopic films emitted by objects to excite the senses, to the incense artisans of ancient Egypt and East Asia, humans have long sought to capture and understand the elusive nature of smell.

Before the emergence of more sophisticated means for extracting and preserving scent, fragrance was elicited through rudimentary methods such as crushing raw botanicals, steeping them in oils, or burning resins to release their aroma.

During the eighth and ninth centuries, the invention of the “modern” alembic — a distillation apparatus developed by Islamic alchemists featuring a still pot, a cooling condenser, and a collection spout — allowed for a more controlled extraction of delicate essential oils than crude crushing or simple heating could achieve. This innovation enabled new forms of fragrance production, introducing alcohol as a base and associating the practice of perfumery more closely with chemistry and medicine. Through trade and translation, this technology and technique migrated to continental Europe, where perfumers expanded their repertoire over centuries with methods such as maceration, expression, tincturing, and enfleurage4 to isolate the volatile compounds of flowers and woods.

In the sixteenth century, tanners making leather gloves sought to mask the acrid smell of their wares with fragrant oils and extracts. Scented gloves quickly became fashionable among the European aristocracy, and perfumers found a lucrative market beyond functional necessity. At Versailles, the epicenter of French culture and seat of royal power, courtly fashion demanded a complete sensory presentation: the right clothing, hairstyles, cosmetics, and an ever-changing repertoire of perfumed products to signal refinement and status.

This high consumption of scent supported a nascent perfume industry, formalized in 1656 in Grasse, France, with the creation of the Maîtres Parfumeurs et Gantier (the perfume and glove-maker’s guild). Alongside its favorable social-political milieu, Grasse’s microclimate fostered a burgeoning perfume industry in the region, where fertile soils nurtured fragrant flowers such as jasmine, rose, lavender, orange blossom, myrtle, mimosa, and tuberose. This economic activity, along with the formation of local perfume, helped establish France’s perfumeries as centers of both craft innovation and the formal study of smell.

The nineteenth century marked a decisive shift as techniques from pharmacy and organic chemistry began to elucidate molecules underlying fragrance. Building on earlier breakthroughs such as the isolation of morphine in 1804 (the first alkaloid ever extracted from a plant), chemists turned their attention to aromatic materials.

In 1820, the French pharmacist Nicolas Jean Baptiste Gaston Guibourt identified and isolated 2H-chromen-2-one, better known as coumarin, from the tonka bean (Dipteryx odorata). In an account presented to the pharmacy section of the Académie Royale de Médecine, Guibourt formally christened the new substance coumarine, marking one of the earliest instances of the chemical characterization of a fragrance compound. In 1858, another French chemist, Théodore Nicolas Gobley, succeeded in crystallizing vanillin from vanilla pods, confirming that odorants could be identified as discrete molecular entities.

For the first time, individual aromatic molecules — a resonant note of the rose, one iota of the vanilla pod — could be extracted from a larger, complex composition. Smell was being recast as a phenomenon amenable to classification and design.

Driven by advancements in organic chemistry and the introduction of the periodic table in 1869, fragrance chemistry blossomed. By 1882, Paul Parquet’s famous scent, Fougère Royale, featured coumarin, followed by Guerlain’s Jicky in 1889, and in 1921, Chanel No. 5 launched using an entirely new class of synthetic compounds, the aldehydes. The perfume industry eagerly adopted new techniques, including chromatography and fractional distillation.

As the twentieth century unfolded, scientists intensified their quest for structural correlates of scent. Discoveries like ionone-related ketones evoking violet and woody notes, long-chain macrocycles recurring in musks, and aromatic rings anchoring vanillic and balsamic tones found their way to the traditional orgue à parfums, a semicircular, horseshoe-shaped work station: a harbinger of what would become a more serious investigation of the science and technology of smell.

Digitizing Smell

Over eons, organisms evolved a sense of smell. In the past three centuries, smell became chemistry. And in recent years, we have started to ask whether smell can become code.

However, unlike sound and color, smell resists straightforward formalization. Color, for instance, has been reduced to three primary channels, standardized through the color wheel, and rendered into numeric systems that machines can interpret. Sound has been decomposed along perceptual axes of pitch, timbre, and amplitude, each capable of digital transformation. Odor, however, has no reliable relationship to molecular structure or perceptual encoding, making it difficult to establish a computational coordinate system.

As a result, early computational efforts in representing molecules were often ad hoc: homemade tables to track atomic bonds, bespoke matrices, or custom linear codes that translated chemical structures into character strings. These methods were clever but small-scale and subjective, making calculations laborious and difficult to reproduce.

Then, in 1988, while at Pomona College in Claremont, California, chemist David Weininger devised SMILES (Simplified Molecular Input Line Entry System). SMILES provided a standardized, machine-readable line notation for encoding molecular structures. Like any language, SMILES is a formal system for representing information; in the context of chemistry, it acts like a cipher or code to translate molecular structures into linear character strings. A given molecule, according to convention, is spelled out as a word or a particular grammatical grouping of letters, where each letter corresponds to an individual atom. Contained in each word is also the logic for how certain letters connect or are arranged geometrically, including instructions for branching and ring closures. For instance, the six-carbon ring cyclohexane is represented by slicing open the ring and labeling the adjacent atoms with matching numbers to indicate connection and closure: C1CCCCC1. In the same fashion, coumarin can be written as O=C1OC2=CC=CC=C2C=C1.

In practice, however, this descriptor-based model could not contend with the idiosyncratic nature of the structure-to-odor relationship: a molecule may be classified as citrus-like by virtue of its ester group, while a structurally analogous compound with only minor modifications might be seen as sharp, metallic, or entirely odorless.

As academic labs continued researching the logic of scent, focus shifted toward building larger datasets that linked molecular structure to qualitative descriptions of odor perception. In place of binary quantifiers such as odorous/odorless or pleasant/unpleasant, these collections captured distinct attributes like fruity, floral, musky, or burnt, offering a more embodied and qualitative relationship between chemistry and experience.

Democratizing databases such as the Good Scents Company, for example, expanded the vocabulary of olfaction available for computation, priming the field for machine learning approaches capable of finding patterns across large, multidimensional datasets.

In 2015, IBM Research and Rockefeller University launched the DREAM Olfaction Prediction Challenge, the first large-scale, open benchmark for predicting human olfactory perception from the physicochemical features of odor molecules. Researchers were provided with data comprising 476 chemically diverse odorants, each described by over 4,800 molecular features and rated by 49 human participants on 19 sensory attributes, such as sweet, fish, mint, and sour.

​​Competing teams trained machine-learning models to map feature-perception relationships and evaluated their models using 69 unseen test molecules. The top models achieved prediction measures comparable to those observed among human participants, meaning the machine ratings were nearly as reliable as human noses when judging whether a chemical smelled floral or fishy. The models’ predictions mirrored the average agreement reported in human odor-perception ratings, demonstrating accuracy of up to 85 percent across multiple different aromas.

Although the DREAM challenge yielded compelling evidence that odor perception could be forecasted computationally, it had its shortcomings. Namely, the study’s dataset remained modest in scale, leaving vast chemical territories uncharted, and its reliance on predefined molecular descriptors meant the models depended on prescribed features rather than uncovering the latent logic linking structure to odor.

By 2019, researchers at Google Brain (now DeepMind) sought to overcome these constraints by expanding both the scale of training data and the fidelity of their model. Using deep learning and Graph Neural Networks (GNNs), a class of models that interpret molecules as graphs with atoms and bonds represented as nodes and edges, respectively, the study employed a dataset containing more than 5,000 odorants annotated by expert perfumers across over 100 descriptors, from mint and potato to sulfurous and grassy.

Unlike the earlier DREAM Challenge, which relied on prescribed molecular features, such as atom counts and topological indices, this approach allowed the model to infer structure-odor relationships directly from data. To initiate the training process, each node (representing an atom) was seeded with basic chemical information, including atomic number, valence, hybridization, and formal charge.

Through a recursive process known as “message passing,” the state of each atom was repeatedly updated in response to information relayed by neighboring nodes. Layer by layer, the model built up a progressively bigger picture of a molecule: early layers learned to identify local features like carbonyls, halides, or ring systems, while deeper layers learned to recognize broader chemical motifs such as aromaticity, conjugation (the overlap of p-orbitals), and steric strain (the increase in potential energy of a molecule due to repulsion between electrons in atoms that are not directly bonded to each other).

By the penultimate layer, the complete, networked “picture” of a molecule was condensed into a fixed-length, 63-dimensional vector, known as an “odor embedding,” capturing the molecule’s perceptual qualities in a computable form. This embedding was then used for classification tasks, such as predicting specific odor descriptors or categorizing the molecule’s scent profile.

When these “images” were compressed, molecules that smelled alike clustered together even when their chemical scaffolds were structurally dissimilar. For example, certain esters and ketones, molecules that share little in common structurally, appeared close in this space because both carried a sweet, fruity scent, while structurally related compounds could be separated if their perceived odors diverged. This act of compression thus exposed a “geometry of smell.”

It also laid the groundwork for Google’s subsequent introduction of the Principal Odor Map (POM): the first map of smell, in which traversing through space corresponds to crossing distinct regions of aroma, from jasmine to potato. Building on the previous study, the researchers expanded the model’s embedding layer by 193 dimensions, creating a high-dimensional coordinate system that positions each odorous molecule as a single point within a continuous manifold (e.g., a connected shape or space that behaves geometrically, enabling meaningful comparison and relation between the position of points representing molecules). In this space, perceptually similar odors occupy nearby positions, much as blue lies closer to turquoise than to crimson on the color wheel, while increasingly dissimilar ones are separated by greater distance.

When the researchers subjected the POM to further tests, they found that it could generalize beyond human olfactory perception, predicting olfactory receptor activity across species from mice to insects. This cross-species application suggests that the model’s internal structure even captures evolutionary principles of scent. On the map itself, metabolically related compounds — those separated by only a few metabolic reactions or naturally co-occurring in the same substance — also occupy nearby coordinates, forming concentrated clusters that reflect their shared chemical and perceptual relationships.

By capturing such subtle perceptual relationships, the model not only surpassed traditional chemoinformatic algorithms in terms of predictive accuracy, but also enabled early steps toward the design of new odorants.

Building on this foundation, Osmo, a start-up spun out of Google Research in 2022, has begun leveraging its proprietary Olfactory Intelligence (OI) platform informed by POM to translate sensory scent data into chemical design. The company’s goal is to “give computers a sense of smell.”

Glossine, Fractaline, and Quasarine are the first prompt-generated fragrance molecules created using its platform. According to the company, Glossine delivers a “Las Vegas-style sparkle,” with a floral jasmine-like top note that adheres well to textiles; while Fractaline offers a versatile violet note, reputed to give a powdery, “second-skin” impression; and Quasarine presents an intense yet delicate jasmine aroma claimed to deliver a long-lasting “fresh petal-y effect.” While these descriptors could be shared by other perfumes, these fragrances are entirely original. Where traditional perfumery relies on the discovery and refinement of proprietary molecules in a process that usually takes years, Osmo can “create” completely new odorants through this OI platform in just a few days.

The potential applications of Osmo’s OI platform, however, extend far beyond fragrance. Because the Principal Odor Map can extrapolate olfaction across species, Osmo has leveraged it for developing synthetic alternatives to DEET, the active ingredient in most commercial insect repellents, but one which has been linked to adverse effects, including severe skin reactions like rashes and welts. Trained on experimental datasets measuring mosquito repellency, the model can predict the repellent efficacy of nearly any molecule. Experimental validation confirmed over a dozen new molecules as repellent as DEET, but which could offer safer, longer-lasting alternatives for killing mosquitoes and ticks.

Beyond repellents, Osmo has broader ambitions to also develop non-invasive diagnostic tools. They aim, for example, to identify volatile signatures emitted by various diseases, enabling algorithms with a “digital nose” to detect conditions such as Parkinson’s, diabetes, and certain cancers through subtle changes in body odor or sebum, a type of signal detectable by dogs.

Perhaps the most promising application of Osmo’s technology, though, relates to sustainability. By synthetically generating fragrance molecules, Osmo offers a path toward decreasing the environmental impact of industrial scent-production. A canonical and increasingly endangered raw material for scents is rose, whose odor has captivated humans for millennia yet remains one of the most labor-intensive and expensive natural ingredients (some 60,000 roses, roughly 180 kilograms of petals, are required to produce a single ounce of oil, which sells for $8,000 to $12,000 per kilogram). By plotting the scent of Rosa damascena and Rosa centifolia on the POM, Osmo can work toward “reverse-engineering” the rose and other floral notes in pursuit of designing “an alternate universe of perfume ingredients” that are perceived similarly without requiring raw botanical sources.

Osmo is not alone in its effort to advance computationally mediated scent. Givaudan’s Carto, the digital design platform of one of the world’s first and largest fragrance houses, is also using computer technology to design its perfumes. Carto integrates predictive algorithms with a database of over 5,000 raw materials (five times more than a human perfumer typically manages) to help perfumers simulate, match, and modify scents. Whereas the classical perfume orgue à parfums once arranged rows of essences within arm’s reach, Carto replaces physical glass vials with a virtual glass touchscreen display. The platform was used to formulate Tom Ford’s Bois Pacifique, which launched in January 2025.

Despite such recent successes, the mysteries of olfaction are far from solved. To digitize the scent of a rose, for instance, requires contending with over 300 volatile compounds that contribute to its spicy, honeyed, and tea-like notes. These compounds are not simply additive but dynamic; their interactions, relative concentrations, and release create emergent qualities unpredictable from any single component alone. While platforms like Osmo and Carto can tinker with individual molecules, capturing the interplay of dozens or hundreds of odorants in a given mixture remains a formidable challenge, the mastery of which will be next in digitizing smell.

Both industry and academia continue to advance this aim. The most recent DREAM Olfaction Challenge, slated to close in late 2025, tasked international teams with predicting perceptual similarity across volatile mixtures. It will draw on a dataset of over 700 combinations containing anywhere from two to ten different molecules to assess how accurately teams can digitally model smells, their interactions, and their resulting impressions. Although peer-reviewed results have not yet been published, early findings point toward improvements in complex-mixture scent prediction.

The Future of Olfaction

Traditionally, the fragrance industry has made a point of drawing a line between the natural and the synthetic, with the introduction of synthetic scent molecules in the mid-nineteenth century garnering both criticism and celebration. Early critics5 proclaimed such synthetic materials as “vulgar debasements” of perfumery, reflecting anxieties surrounding industrialization and the loss of heritage and craftsmanship. But others celebrated this innovation. Guerlain’s Jicky (1889), for instance, which incorporated synthetic vanillin and coumarin, was hailed as a new chapter for perfume. Moreover, commercial houses like Lubin marketed synthetic musks as “triumphs of science … over Nature,” promoting the “non-evanescence” (long-lasting) qualities of synthetic chemicals in comparison to natural ingredients.

These developments unfolded within a wider cultural moment that the essayist Max Beerbohm described as “a new epoch of artifice.” The emergence of synthetics did not simply replace the natural; it upset the very idea of what “naturalness” meant — did it refer to an ingredient’s source, its sensory impression, or the meanings attached to it?

Even today, materials such as ambergris (a waxy, sweet-smelling substance formed in the digestive system of sperm whales and expelled into the ocean) remain highly coveted precisely because of their scarcity and natural origins. Revered as “the treasure of the sea,” ambergris is found in less than five percent of sperm whales and develops its celebrated complexity over years of exposure to sea, salt, and sun. Such a valued ingredient commands reverence precisely because of its rarity, exposing how ideas of purity and authenticity continue to shape our perception and appreciation. Ultimately, the persisting popularity of ingredients such as ambergris demonstrates that value pertains as much to culture as to chemistry, reflecting not only the reality of raw materials but also the moral and aesthetic weight we ascribe to their provenance.

Given this legacy, how might we relate to machine-generated molecules?

The shift to digitized scent will require that we rethink not only the substances themselves, but also the stories we tell as we find ways to valorize their synthetic origins. Such computationally-designed scents are, after all, safer, allergen-friendly formulations compliant with evolving regulations. Furthermore, AI-designed aromas often use more sustainably produced molecules, with a lab-created civetone replacing wild civet extract (a substance associated with the questionable practice of keeping civet cats in captivity for their perineal gland secretions).

A similar parallel has played out elsewhere: a one-carat lab-grown diamond, while chemically and optically identical to a mined one, can cost less than a quarter of the price, despite being purer and more ethically produced. While they have been derided as “costume jewelry,” the market for lab-grown diamonds was valued at more than $18 billion in 2023 and is expected to continue growing. The connotations of luxury are increasingly leaning toward narratives of sustainable and ethical sourcing.

Machine-imagined scents may follow a similar arc. But just as the telescope widened our aperture to distant cosmic structures, digitally composed scents will expand our olfactory range, this time towards the smallest scales of chemical configuration.

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Taylor Rayne holds a degree in biochemistry and computer science, as well as a deep curiosity for the interplay between scientific and cultural production. She currently works at the Novo Nordisk Foundation Center for Biosustainability, based at the Technical University of Denmark.

A special thanks to Christiana Agapakis for her generosity and resources; Jasmina Aganovic for her thoughtful guidance and time; Xander Balwit for her steady editorial support, and of course, Astrid.

Cite: Rayne, T. “Scent, In Silico.” Asimov Press (2026). DOI: 10.62211/28jw-12ty

By Ralph Stefan Weir

On 1 November 1837, Charles Darwin delivered a talk to the Geological Society of London on the role of earthworms in soil formation. The Society is said to have expected something grander from the celebrated scientist, but Darwin was already deeply fascinated by worms. Indeed, his interest intensified throughout his life and served as the subject of his final book, The Formation of Vegetable Mould Through the Action of Worms, published in 1881.

Darwin’s book is noteworthy not just as the first major text on bioturbation (the reworking of soils by organisms) but also for how he approaches the inner lives of earthworms:

Judging by their eagerness for certain kinds of food, they must enjoy the pleasure of eating. Their sexual passion is strong enough to overcome for a time their dread of light … Although worms are so remarkably deficient in the several sense-organs, this does not necessarily preclude intelligence … and we have seen that when their attention is engaged, they neglect impressions to which they would otherwise have attended; and attention indicates the presence of a mind of some kind.

Darwin was not the first scientist to reflect on animal sentience, that is, their capacity for pain and pleasure. Aristotle wrote extensively on the topic, observing, for instance, that “bees seem to take pleasure in listening to a rattling noise” and that “the tunny delights more than any other fish in the heat and sun.”

Until the nineteenth century, such observations remained anecdotal. Darwin was among the first to ground judgements about animal sentience on careful experiments, such as suspending pieces of raw and roasted meat over the worms’ habitat overnight to see which they preferred.1

Even more striking than Darwin’s methodological approach to studying sentience was his choice of earthworms for his subject. Such a selection in place of a human subject made Darwin a forerunner of a research program that has recently gained incredible momentum: the science of borderline sentience. That is, the investigation of sentience in creatures that dwell near the boundary between sentience and non-sentience.

Whereas Darwin’s interest in the inner workings of the worm mind was driven by pure curiosity, researchers today study borderline sentience to avoid causing gratuitous suffering in contexts such as agriculture and research. In the UK, octopuses and decapod crustaceans have been recognized as “sentient” since 2021, meaning government ministers legally must consider their welfare in future policies. This has just resulted in a ban on the practice of boiling crabs and lobsters alive.

The same considerations also apply to humans. Every year, around 400,000 people fall into “prolonged disorders of consciousness,” such as a coma, due to injury or illness.2 While no longer recognizably sentient, as many as a quarter of these patients are thought to retain some awareness. The better we understand borderline sentience, then, the better we will be able to care for (and perhaps even cure) such individuals.

Indeed, misjudgments about sentience can have grave consequences. Before the 1980s, it was common practice to perform surgery on newborns without anaesthesia, partly due to the assumption that neonates do not experience meaningful pain. This changed in 1987, driven by mounting physiological evidence (such as electrical activity in the cortex, sharp increases in stress hormones in blood samples, and the microscopic structures of developmental brain tissues) of the capacity for pain sensation in infant brains, alongside campaigns by mothers whose children were subjected to such treatment.3

Fortunately, rapid advances in neurophysiology are allowing us to make judgments about borderline sentience that would have seemed impossible a few years ago. Tools like high-resolution functional MRI (fMRI), calcium imaging, and high-density electrode arrays can now help us observe detailed neural activity in real time and correlate specific patterns with conscious states. The field of connectomics, which attempts to map the complete wiring diagram of neural systems, also promises to reveal the fine-grained physical processes underlying sentience in humans and other creatures.

Studies of the microscopic worm C. elegans, with its fully mapped and readily accessible nervous system, have become ideal test cases for assessing theories of sentience against detailed physiological data. The hope is that discoveries made with this species will help refine how we assess sentience in humans, other complex animals, and even artificial neural networks.

Borderline Sentience

While sentience is often defined as “the capacity for pain and pleasure,” this definition isn’t complete. Sentience, in the sense we are using the term, is a combination of two things: consciousness and valence. To say an organism is conscious means that there is “something it is like to be that organism”; that it experiences the world from its own subjective point of view. That is how philosopher Thomas Nagel puts it in his famous paper, “What is it Like to be a Bat?”4

“Valence” is short for “hedonic valence,” from “hedone,” the Greek word for “pleasure.” To say that a conscious experience is valenced is to say that it is pleasant or unpleasant, that it feels good or feels bad. Toothache, breathlessness, and nausea are examples of negatively valenced experiences, whereas things like euphoria, flow state, and the sensation of quenching one’s thirst are all examples of positively valenced experiences.5

Not all conscious experiences have significant valence, however. The visual experience of seeing a brick wall, for instance, may feel neither good nor bad. Some scientists have even suggested that there may be conscious creatures that lack valenced experience. For example, Simona Ginsburg and Eva Jablonka speculate that certain ancient animals, such as jellyfish, might experience a meaningless “white-noise sensation”— an inner buzzing and crackling arising as a side-effect of their decentralized nervous systems.

Valenced experience, if and when it does exist, however, has tremendous practical importance. This is because many (some would say all) practical decisions are ultimately about increasing positive experiences and decreasing negative ones. When we decide whether to go on holiday in England or the Galápagos, we choose the place we expect to enjoy most. When we arrive at the ward where our Grandma has been hospitalized, we are concerned about whether she is comfortable and free from distress. And when we decide whether to permit scientists to inflict spinal injuries on rats to test a neural regeneration drug, we weigh the potential value of this work against the suffering it will cause the test animals.

Sentience, then, is the combination of subjective experience and the capacity to evaluate sensation as good or bad.

While this might sound deceptively simple, sentience poses formidable challenges to scientists because there is a vast range of questionable, borderline cases. Examples include humans (such as those with brain injuries), non-human animals (such as insects or fish), and some creatures that are neither humans nor animals (such as neural organoids and AI).

Representatives of the first category include people with prolonged disorders of consciousness and those in early developmental stages. Before the 1970s, patients with disorders of consciousness were frequently grouped together as “non-responsive” or “comatose.” In 1972, physician-scientists Bryan Jennett and Fred Plum established the diagnostic category persistent vegetative state for unresponsive patients who exhibit sleep-wake cycles and “autonomic” functions such as respiration, digestion, and pupil dilation, though they are traditionally thought to lack awareness.6

Human babies are another example. Here, research on developmental phases has led us to abandon the assumption that newborn infants lack significant sentience and replace it with an understanding of the neural processes thought to underlie experiences of pain and pleasure starting at 12 weeks’ gestation. When, exactly, sentience arises is still up for debate (partly because of disagreement about whether sentience in humans rests essentially on activity in the cortex), but it has similarly enormous implications.7

When it comes to non-human animals, views about which creatures are sentient diverge even more. At one extreme are those held by the neuroscientist Edmund Rolls, who attributes sentience only to organisms with distinctively primate neural mechanisms, the granular prefrontal cortex in particular. At the other end are those held by cognitive psychologist Arthur Reber, who argues that even single-celled organisms such as bacteria may be sentient. Most scientists fall somewhere in the middle. There is a broad consensus that mammals, birds, and octopuses are sentient, and that single-celled organisms are not, but considerable disagreement beyond these cases.

The last category of borderline-sentience is non-human non-animals, such as human neural organoids and deep neural networks.8 A human neural organoid is a lab-grown tissue derived from human stem cells grown in a culture that allows them to differentiate into various neural cell types that mimic those of the brain.

Neural organoids offer great potential for advancing neuroscientific research without the need for invasive experimentation on humans or other animals. At the same time, the pioneer of “neuroethics,” Andrea Lavazza, has expressed concern that in growing something like a portion of human brain tissue, we might unwittingly be creating something like a portion of human mind, capable of positive and negative experience.

Deep neural networks fall into a similar category. These are the kind of computer architectures that underlie all the recent advances in artificial intelligence, from video generation to chatbots. Like organoids, they are inspired by the structure of the nervous system and are thought to have some analogous functions.

A group led by Patrick Butlin and Robert Long argues that existing deep neural networks satisfy some nontrivial indicators associated with influential (though contested) computational theories of consciousness. For example, the transformer networks that drive chatbots have some of the features proposed by the “global workspace theory,” according to which conscious states arise when information is broadcast across a system so that many specialized processes can access and use it.9

Butlin and Long’s “indicators” for consciousness drive at something extremely important for machine consciousness, animals, and humans alike: the question of how we can know sentience when we see it.

The Limits of Behavioral Evidence

Conscious experiences are private in the sense that they are not directly observable from the outside. When it comes to healthy adult humans, this does not pose too great a problem. If a research psychologist wants to know what a patient is experiencing, they can ask. It would be handy if we could do the same with earthworms, but regrettably, they can’t speak. The same is true for comatose humans and neural organoids. And while we can ask a chatbot or a parrot what it’s experiencing, their answers are of little use as evidence, given that they have been trained to produce human-like responses without necessarily possessing the underlying subjective experiences those responses typically indicate.10

This all goes to say that studying borderline sentience forces researchers to seek out and validate markers of sentience other than the subjects’ verbal report.

The most frequently substituted markers are non-verbal behaviors.11 These range from comparatively simple things, such as avoiding harm or guarding an injury (e.g., pulling an injured paw near a body), to more sophisticated behaviors such as self-administering painkillers or making motivational trade-offs (for example, the way in which worms, according to Darwin, experience sexual desire strongly enough to overcome their dislike of light). Indeed, in the mid-twentieth century, radical “behaviorists” led by B. F. Skinner held that all of psychology could, in principle, be explained in terms of observable behavior.

Behavioral markers of sentience are frequently unsatisfactory, however, as sentient creatures may fail to exhibit the usual behavioral signs for a variety of reasons. Someone with cognitive motor dissociation, for example, can have a substantial inner life without exhibiting any outward signs of it.

This is what happened to Kate Bainbridge, a 26-year-old woman who lost responsiveness due to inflammation of the brain and spine, triggered by a viral infection. Although she was diagnosed as being in a persistent vegetative state, she later regained the ability to communicate via keyboard. When she did, she reported that she had remained aware, deeply scared and uncomfortable, through much of the time that she was believed to be “unconscious,” undergoing painful procedures such as airway suctioning without doctors having taken the time to explain their purpose to her due to her perceived unresponsiveness.12

Furthermore, behaviors that provide evidence of sentience in creatures that are assumed to be capable of it can provide poor or misleading evidence in certain contexts. Consider the rat-grimace scale. Developed in 2011 by neuroscientist Jeff Mogil, the scale is a tool for assessing whether rats are in pain by their facial expressions, employing four “action units” (squinting, cheek flattening, ear-changes, and whisker movement). The assumption that underlies the scale is that rats exhibit reflex facial movements in reaction to nociception, or the detection of harmful influences. And nociception is, under ordinary circumstances, good evidence for pain in animals capable of pain.

However, because these facial responses are reflexes, they are not themselves good evidence that rats have the capacity for pain in the first place. In other words, the rat’s nervous system would produce them even if pain were absent. In fact, it is now widely agreed that any behavior that counts as evidence of sentience in creatures capable of such experience could also be exhibited by creatures incapable of, or not currently undergoing, sentient experience.

For example, a sleepwalker can navigate their house, unlock doors, and make a snack without any awareness, just as a conscious person might do the same while fully awake This ability has impacted a number of criminal trials, such as that of a Canadian man, Kenneth Parks, who was acquitted of murdering his in-laws on the ground that he carried out the actions while sleeping.

One way to reduce our uncertainty about behavioral evidence for sentience is to appeal to evolutionary proximity. Because humans are sentient, there is reason to think that this is also true for creatures closely related to humans, including other mammals, such as rats. In this view, the rat grimace scale is probably reliable (rats are, after all, used in the laboratory because of how their biology models that of humans). However, this does not help with cases where the potentially sentient creature is not closely related to us, as with insects or octopuses, or cases where the behavioral evidence is absent or ambiguous, such as with sleepwalkers or neural organoids.

In these cases, we need some other way of differentiating between behaviors that seem sentient and those that really are — perhaps, by looking under the surface.

The Contribution of Neurophysiology

The reason we can be more confident about sentience in creatures more closely related to us is not prejudice in favor of our more winsome mammalian cousins but because of morphological similarity (“homology”). In other words, a rat’s grimace is better evidence of pain than that of an AI avatar because it was produced by a brain similar to our own. Humans and rats share brain regions known as the anterior cingulate cortex and the nucleus accumbens, which are known to play a role in human pain. These regions have been shown to exhibit similar activity in response to the same cause (for example, a hot surface applied to the back of the hand or paw).

As our understanding of neurophysiology grows, we are increasingly able to base our judgments about sentience directly on the physical systems involved rather than proxies like language or behavior.

A great deal of this increased understanding owes itself to advancements in technology, such as fMRI. A landmark 2006 investigation led by the neuroscientist Adrian Owen sought signs of awareness in the brain of a 23-year-old woman who had entered a vegetative state after sustaining severe brain damage in a traffic accident. The investigators asked her to perform two mental imagery tasks known to activate spatially distinct brain regions in healthy individuals: imagining playing tennis and imagining walking around her house. Amazingly, fMRI scans revealed brain activities nearly identical to those observed in healthy subjects. Owen and his colleagues concluded that the woman was conscious and capable of voluntary mental activity.

Subsequent studies reproduced this result, leading to the establishment of “cognitive motor dissociation” (CMD) as a clinical category for patients who are conscious but incapable of voluntary physical movement. One 2010 study even identified a patient capable of correctly answering autobiographical yes-or-no questions by performing the same mental imagery tasks, raising the prospects of clinical applications not just in diagnosis but also in restoring communication.

As impressive as functional imaging approaches to borderline sentience are, however, they are relatively coarse-grained.13 The spatial resolution of fMRI is limited to millimetres cubed, hundreds of thousands of neurons, and reflects slow changes in blood oxygenation rather than neural firing itself. EEG, a noninvasive test that records the brain’s electrical activity via electrodes placed on the scalp, has better temporal resolution but even lower spatial resolution. These methods are valuable for observing large-scale patterns of neural firings, but they leave out vast quantities of detail in the brains of large animals like humans.

When it comes to smaller animals, the situation is even worse. A fruit fly’s brain, for example, is made up of about 140,000 neurons in a 0.1mm cubed space, meaning that even a state-of-the-art fMRI has a resolution larger than a fly’s brain. If a fruit fly flew into an fMRI scanner and kept still long enough, all we would see is a faint, undifferentiated signal — far too coarse to distinguish even the broad outlines of its brain, let alone the activity of individual neurons.

Fortunately, more precise methods of interrogating the brain structures suspected to be involved in consciousness are becoming available.

For mammals, there are two theories about which region of the brain (cortical or subcortical) is thought to give rise to consciousness. The first theory says that human sentience derives entirely from processes involving the neocortex, the furrowed outer layer of the brain that expanded rapidly in primate evolution and is especially large in humans. This casts doubt on insect sentience, since it suggests that sentience is unique to creatures with a neocortex (only mammals), or something like it (the bird pallium, perhaps).

An alternative theory that has gained ground recently attributes some sentient processes to subcortical activity in the midbrain. An important source of evidence for this theory is that children born with little or no neocortex (a rare condition known as “hydranencephaly”) retain some abilities which, in healthy humans, involve consciousness.

Another data point comes from experimentally “decorticated” mammals. Decortication is a nasty process in which the cortex of a living mammal, usually a cat or a rodent, is surgically removed or destroyed. Few ethics boards would approve such experiments today. But past results suggest that decorticated animals also retain abilities, such as visual orientation, self-defence, and social play, that are ordinarily associated with consciousness. The neuroscientist Bjorn Merker draws on this evidence to argue that core conscious experiences depend mainly on a midbrain system that generates a subjective representation of the animal in its environment without relying on the cortex.

Until recently, neither of these theories had much bearing on the question of insect sentience. There was simply no evidence that insects had anything like the cortical or midbrain structures upon which the competing theories of consciousness focus. Instead, researchers supposed that insect behavior was governed by chains of local reflex circuits, strung along the body, with only minimal coordination from the brain. If so, we would have little reason to think of insect behavior as any more conscious than human reflexes.

However, a 2016 study by neuroethologist Andrew Barron and philosopher Colin Klein suggests this is wrong, arguing persuasively that the insect brain is actually strikingly analogous to the mammal midbrain.

Barron and Klein draw on an impressive range of evidence to make their case. In a particularly compelling study from 2015, a fruit fly is attached to an arm to keep it in place atop a polystyrene ball, suspended by a stream of air. When the fly walks, the ball acts like a treadmill that can rotate in any direction. Its movements control a virtual environment that the fly can navigate. As it does so, its brain activity is monitored by means of two-photon calcium imaging.

Two-photon calcium imaging works by using laser light to excite fluorescent proteins inside neurons, making them glow more brightly as calcium levels rise, a proxy for neural firing. This allows researchers to observe the activity of thousands of individual neurons in real time, far surpassing the spatial and temporal resolution of fMRI.14

What the study found was that a part of the fly’s brain known as the central complex integrates information about the animal’s movements and orientation in space, generating an internal compass-like representation which it uses to navigate. Flies do not merely move by chaining together reflexes triggered by their immediate surroundings but maintain a continuous representation of their orientation and trajectory within their environment, updating it as they navigate.

Given this, and other evidence, Barron and Klein argue that the insect brain as a whole is, in fact, functionally analogous to the vertebrate midbrain.15 The central complex in insects serves the role of the vertebrate superior colliculus, processing spatial information for navigation; the insect mushroom bodies perform the functions of the vertebrate basal ganglia, facilitating memory-based action selection, and so on.

From this, we can imagine that if that subsystem is sufficient to determine consciousness in us, then the insect brain is probably sufficient to say it, too, possesses consciousness. If the midbrain theory is correct, then we have good reason to think that not only all vertebrates but also insects are sentient as well.16 This result challenges the consensus against insect sentience and raises uncomfortable questions about their treatment in insect farming and the wild.

The Worm as Standard-Bearer

Barron and Klein’s work, and the experimental research they draw on, would have astonished Darwin. However, they are still focusing on comparatively high-level functional analogies between insect and mammalian brains in their quest to investigate indicators of sentience.

To fully understand the physiological evidence concerning borderline sentience, we need to properly exploit the neural-level data to which we increasingly have access. This brings us to the fast-growing field known as connectomics, which aims to understand the brain at the scale of individual neurons and their connections.17

Tracing the precise interconnections of neurons is a formidable task. After all, neurons are densely packed, morphologically complex, and connected by vast numbers of gossamer-thin electric cables called “neurites.”18 Understandably, connectomics’ pioneers chose to start simple — they, like Darwin, turned to the worm.

However, they did not use the earthworms that so interested Darwin, but Caenorhabditis elegans (C. elegans), a microscopic nematode. Nematodes are believed to have changed relatively little since they first emerged 500-600 million years ago. That is (probably) around when centralized nervous systems first developed, and nematodes are among the earliest creatures to possess them. By studying nematodes, we can gain insight into the primordial origins of the brain. Perhaps more helpful, however, is that C. elegans’ nervous system contains just 302 neurons (compared to our 86 billion), making it a perfect model organism for connectomics.

A major milestone came in 1986, when Sydney Brenner’s research team at the MRC Laboratory of Molecular Biology in Cambridge published a detailed wiring diagram of the C. elegans nervous system. The result of an extraordinary effort, it required fixing the worm in osmium tetroxide (a highly toxic oxidizing chemical), sectioning it into several thousand ultrathin slices, and scanning these slices under an electron microscope. The researchers then manually traced neurons and synapses across thousands of images to create the complete map. Where sections were damaged, incomplete, or ambiguous, data from other worms were gathered to fill the gaps.

For decades, the value of this C. elegans connectome was primarily indirect, catalyzing advances in electron microscopes, image analysis, and reconstruction techniques that could help with more ambitious connectomics efforts. Only very recently has it become the subject of physiological research explicitly aimed at investigating sentience.

So far, attention has focused on one topic in particular: the challenge C. elegans poses to the important behavioral indicator of sentience known as motivational trade-offs. These involve the weighing of different drives to optimize behavior.

For many years, researchers have treated motivational trade-offs as especially strong evidence of sentience. After all, they occur when a creature balances different dispositional drives, such as the drive for nourishment or the drive to avoid harm, to optimize behavior. Earlier, we saw an example in Darwin’s observation that earthworms’ desire for sex appears to outweigh their dislike of light.

The French-born Canadian psychologist Michel Cabanac has been researching the role of pain and pleasure in guiding the behavior of animals since the 1960s. After several decades’ work, he advanced what would become an influential theory according to which sentience developed specifically to facilitate such trade-offs. Behaving organisms, Cabanac proposed, require a “common currency” to weigh and rank different motivational drives. Valenced experience provides that currency.

Cabanac showed that apart from its common-sense appeal, his conjecture makes accurate predictions about humans and other sentient creatures under experimental conditions. For example, human subjects tolerate cold or muscular pain for longer when offered a greater monetary reward, choosing to end the task only at the point when the discomfort outweighs the anticipated pleasure of payment. He subsequently expanded this theory, proposing that sentience first emerged in amniotes, the common ancestors of birds, mammals, and reptiles, around the close of the Paleozoic Era (c. 200-300 million years ago), and arose to make motivational trade-offs possible.

As it turns out, motivational trade-offs are more widespread in the animal kingdom than even Cabanac’s expansive theory suggests. Hermit crabs, for example, appear to evaluate many different motivational trade-offs in choosing a new shell, such as size, camouflage potential, and the pugilistic prowess of the current occupant. And in 2022, a study led by Lars Chittka at Queen Mary University, London, showed bumble bees make comparably sophisticated trade-offs weighing the benefits of high-quality food against exposure to harmful heat, resulting in a spate of articles in venues such as IFL Science, Scientific American, and Vox announcing that bees feel pain.

The new examples already strain Cabanac’s theory. If creatures as seemingly simple as crabs and bees can manage trade-offs, perhaps this marker is not as distinctive of sentience as we had hoped. The revelation that C. elegans does the same, and a detailed understanding of how it achieves this, may prove the final straw to upend it.

For their tiny size, nematode worms are surprisingly sophisticated. If you place a damaging fructose or cupric ion barrier between a worm and an odorant that signals food, it will weigh up factors including the strength of the harmful substance, the strength of the odorant, and when it was last fed to determine whether to brave the barrier. Worms are bolder where the barrier is less concentrated or the odorant more so, and well-fed worms are choosier about which food sources they pursue. Likewise, worms are less fastidious about the repellent octanol when food is available. In other words, nematodes make what look like smart — conscious — motivational trade-offs.

At face value, this intelligible weighing of interests might be treated as reason to think that nematodes have valenced experience, pushing the origins of pain and pleasure back 200 million years earlier than Cabanac’s amniote theory. Some researchers are willing to entertain nematode sentience. But others draw the opposite conclusion. For example, a 2020 paper by the philosopher Elizabeth Irvine proposes that the C. elegans nervous system, with its 302 neurons, is too simple for consciousness, and that there must therefore be something wrong with the idea that such behaviors provide good evidence of the capacity for sentience.

Irvine draws this conclusion from the overall simplicity of the C. elegans connectome, principally the small number of neurons and connections that make it up, rather than the specific organization of those cells for complex behaviors. A more recent paper by Oressia Zalucki and colleagues at the University of Queensland’s School of Biomedical Sciences attempts something more challenging. Alongside the philosopher Deborah Brown and neuroscientist Brian Key, Zalucki sets out to identify the specific neuronal circuitry underlying motivational trade-offs in C. elegans. Her stated aim is to identify the “minimal neuronal circuitry needed to generate subjective experience” (in effect, determine whether nematodes are sentient).

Finding the precise neuronal circuitry driving a behavior means taking connectomics beyond static structure to dynamic functions. The basic methodology consists of identifying neurons that are necessary for a behavior (whose loss impairs it) and those that are sufficient for the behavior (whose stimulation triggers it). Since the 2010s, this has usually been achieved by optogenetics, which allows individual neurons to be activated or silenced in response to light by genetically engineering them to express light-sensitive ion channels. Other methods include laser ablation and electrical stimulation. Researchers can thereby seek to identify the entire circuit underlying a behavior. The C. elegans touch-withdrawal and egg-laying circuits are two classic examples identified in earlier research.

Zalucki and her colleagues attempt to do the same thing for the trade-off a worm makes when it detects the noxious chemical octanol in the direction of a potential food source. In food-rich conditions, the worm briefly turns tail before returning to seek more food; when hungry, it hesitates longer before retreating but sticks with the decision longer once made. Drawing on a wide range of prior studies, Zalucki identifies a circuit of two sensory neurons and three interneurons (those that fall between sensory and motor neurons) that facilitate this trade-off. The two sensory neurons detect the competing influences of food and octanol, two interneurons modulate the worm’s response, and a third interneuron signals the command to motor neurons.

The circuit identified by Zalucki has two features that are relevant to the relationship between motivational trade-offs and sentience. First, even for the 302-neuron nematode, this 5-neuron circuit is extremely simple. Secondly, there is nothing in the functional organization of the circuit to distinguish it from the kind of unconscious reflex circuits that have been reconstructed, albeit less exhaustively, in studies of mammals. For example, similar structures have been observed to mediate the stretch reflex in mammalian spinal cords, as well as unconscious processes in the retina and primary visual cortex.

Zalucki’s findings are physiologically unremarkable; after all, few would be surprised to find that C. elegans’ behavior is achieved by a simple circuit of the kind they identified. But the implications for the connection between motivational trade-offs, a classic behavioral marker of sentience, are significant.

First, if simplicity counts against sentience, as most researchers agree it does, then the great simplicity of the circuit underlying this trade-off counts against its being sentient. Secondly, and perhaps more importantly, if similar circuits in mammals are known to mediate unconscious reflexes, then it seems reasonable to suppose that the nematode circuit operates unconsciously, too.

Like Irvine, Zalucki argues against the notion that motivational trade-offs are evidence of sentience. But others are more agnostic. A recent paper by Simon Alexander Burns Brown and Johnathan Birch proposes that rather than abandon the idea of motivational trade-offs as evidence of sentience, we should refine it, adding other criteria such as the “prospective weighing of risk and opportunity, integration of information from many different sources.” Either way, it is clear that motivational trade-offs are not by themselves the first-rate evidence of the capacity for sentience they have sometimes been taken to be.

While challenging the notion of motivational tradeoffs as evidence of sentience is impressive in its own right, this is not even the most remarkable thing about Zalucki’s finding. It is that she did it by investigating the question, for the first time, at the level of individual neurons.

The Future

Something notable about both Zalucki’s and Barron and Klein’s work is that they draw conclusions about borderline cases by contrasting them to the paradigmatic case of healthy adult humans. This is likely to remain central to the field’s methodology. For this reason, our ultimate goal should be to seek out the same kind of neuron-scale structural and functional understanding of the human brain that we have of nematodes.

This is a tall order. While connectomics research is advancing, it’s an extremely nascent field. In terms of truly complete, neuron-to-neuron wiring diagrams of an entire nervous system, we’re still limited to a handful of relatively small invertebrates (C. elegans, Drosophila, and a couple of marine larvae). The jump from fruit fly (~140,000 neurons) to something like a mouse brain (~70 million neurons) or human brain (~86 billion neurons) remains an enormous technical challenge.

This challenge is compounded by the fact that mammalian brains are not just larger and more complicated than those of nematodes and fruit flies; they are also much more variable. The nematode and fly brains are highly stereotyped, meaning that evidence from one sample has great value for understanding the whole species. This is not possible to the same degree for other animals. An accurate map of your brain would differ in important ways from that of another human. In fact, due to plasticity and cell turnover, it would even differ from your own a few years before or after such a study was done.

Even if we were able to draw a full map of neural connections for individual human brains, it isn’t clear that the neuronal level is fine-grained enough to give us a complete picture of sentience. The idea that the neuron is the “functional unit” of the brain suggests that we can understand the distinctive activities of the brain while setting aside finer detail. Increasingly, however, researchers see smaller components as making a non-negligible contribution, from glial cells to molecular concentrations and even, on some radical views, quantum effects in microtubules. The more that research suggests that smaller-scale entities influence brain processes, the more difficult it will be to gather all the physiological evidence that bears on questions of sentience.

The perception that the nematode nervous system is a simple mechanism because it has only 302 neurons itself holds only to the degree that complex subcellular processes do not significantly modulate its functioning. This assumption might be deeply mistaken. There exists a longstanding project to emulate the nematode nervous system in a computer that can operate a robotic worm body. This project, known as OpenWorm, has proven remarkably difficult to solve. After 15 years’ effort, it still remains a work in progress, reflecting how little we really understand even this paradigmatically simple nervous system.

Setting aside the uncertainties that surround the nascent field of connectomics, there remains significant disagreement over more established neuroanatomy and physiology. For example, the midbrain theory of sentience, on which the whole of Barron and Klein’s theory of insect sentience depends, is itself controversial. Brian Key, the senior contributor to Zalucki’s paper, is one of the most forceful opponents of the midbrain theory, arguing that human sentience depends on distinctively mammalian cortical structures, and that even many vertebrates, fish in particular, are therefore unconscious. There exist formidable methodological difficulties in adjudicating this disagreement.19 The problem only grows when we move beyond organisms to the possibility of machine consciousness, where we lose even the modest guidance offered by common biology.

This is troubling, as so much rides on getting our theory of the neural correlates of sentience right. We look back with horror now at the practice of conducting surgery on infants without anaesthesia. Until the early 2000s, patients diagnosed as “permanently vegetative” were commonly denied attempts at rehabilitation, medical care, or even food and water, on the assumption that there was “no one there.” If, as we now think, even a small fraction of these patients were aware, these protocols may have been unknowingly barbaric.

Yet, excessive credulousness about sentience also carries real costs. For example, animal ethicist and activist Gary Francione points out that defenders of plant sentience risk undermining the rationale behind protections for animals. After all, the idea that even plants have feelings suggests that we need not provide greater protection to cats and cows than we do to the grass beneath our feet. Likewise, when Blake Lemoine lost his job at Google for claiming their chatbot had feelings, it was both bad for him and awkward for his employer. Furthermore, if he had been successful in convincing others, the consequences could have done incredible damage to the entire AI industry. Genuine reasons to think AIs are conscious might make this an acceptable sacrifice, but a misguided belief that chatbots feel could be economically disastrous.

In the same way, if there is a serious chance that insects are sentient — and it seems there is — then we have a moral obligation to rethink how we treat them. But falsely assuming that insects require sentience-based consideration could impose a massive and unnecessary cost on scientific research and the large and growing insect food industry.

There is no shortcut for addressing these challenges, only a desperate need for more research. This will require additional connectome maps and experimental evidence linking them to the kinds of processes, such as motivational trade-offs, that have been taken as proof of sentience. A good first step would be to identify the neural circuitry underlying trade-offs in nematodes other than the food-octanol example that Zalucki investigates. We might move from there to more complex organisms and to other sentience markers, always combining fine-grained connectomics data with more coarse-grained physiological and behavioral evidence.

There is a vast distance to cover before we reach anything like the ideal goal of understanding large mammalian brains at a neuronal scale, but even partial progress could yield substantial payoffs. A better scientific understanding of borderline sentience could help unlock technologies that influence or are controlled by mental states. Promising applications include neuro-prosthetics that restore functions lost through illness or injury, as well as new alleviants such as painkillers and anti-depressants. Technology companies are already exploiting these advances to develop impressive new products such as Neuralink’s brain-computer interfaces or Vertex Pharmaceuticals’ breakthrough non-opioid painkiller. Likewise, researchers in this field are already having a real-world policy impact. Johnathan Birch was able to convince the UK government to recognize cephalopod sentience using a range of existing behavioral and physiological evidence.

Ultimately, investigation into borderline sentience remains both technically and scientifically challenging. Yet for those of us who share Darwin’s curiosity about the frontiers of mind and experience in worms, bats, and other creatures, the path forward is not just practically important but also intellectually fascinating.

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Ralph Stefan Weir is a philosopher at the University of Lincoln. He also writes for Works in Progress and Psychology Today.

Acknowledgments: Thanks to Jun Axup for providing feedback on an earlier version of this draft, to Lauren Kane and Sebastian Seung for valuable conversations, and to Xander Balwit for contributing to the development of this piece. Lead image by Mariya Khan.

Cite: Weir, R.S. “What It’s Like To Be A Worm.” Asimov Press (2026). DOI: 10.62211/27hw-58nw

I first heard people seriously discussing the prospect of “running” a brain in silico back in 2023. Their aim was to emulate, or replicate, all the biological processes of a human brain entirely on a computer.

In that same year, the Wellcome Trust released a report on what it would take to map the mouse connectome: all 70 million neurons. They estimated that imaging would cost $200-300 million and that human proofreading, or ensuring that automated traces between neurons were correct, would cost an additional $7-21 billion. Collecting the images would require 20 electron microscopes running continuously, in parallel, for about five years and occupy about 500 petabytes. The report estimated that mapping the full mouse connectome would take up to 17 years of work.

Given this projection — not to mention the added complexity of scaling this to human brains — I remember finding the idea of brain emulation absurd. Without a map of how neurons in the brain connect with each other, any effort to emulate a brain computationally would prove impossible. But after spending the past year researching the possibility (and writing a 175-page report about it), I’ve updated my views.

Three recent breakthroughs have provided a path toward mapping the full mouse brain in about five years for $100 million. First, thanks to advances in expansion microscopy, we can now “enlarge” the brain to twenty times its normal size using a swellable polymer. This makes it far simpler to image neurons and trace their connections using light rather than electron microscopes. Second, E11 Bio (a nonprofit research organization) recently developed protein barcodes, stained with colorful antibodies that, when delivered into brain tissue, cause each neuron to light up in a distinct color. This makes tracing them much easier. And third, Google Research released PATHFINDER last May, an AI-based, neuron-tracing tool that can proofread about 67,200 cubic microns of brain tissue per hour, with very high accuracy.

These technical advances are just one part of the “brain emulation pipeline,” and scaling these methods to human brains may still prove a challenge. But given these breakthroughs and other trendlines, I now find it plausible that readers of this essay will live to see the first human brain running on a computer; not in the next few years, but likely in the next few decades. This computational brain emulation won’t just be an abstract mathematical reconstruction, either, but rather an accurate, digital brain architecture represented in a virtual body that behaves indistinguishably from our own flesh-and-blood brains.

Such an achievement would have enormous real-world value. When I began researching brain emulation, my motives were primarily centered around constraining risks and harms from advanced AI. I thought that, if only we could directly impart thought and behavior from our brains into AI models, then perhaps they would act in greater alignment with our own values. Today, I am less certain about this assumption, given the velocity of AI development. But there are many other (potentially even greater) value propositions for brain emulations.

Many drugs, materials, and methods, for example, are created by identifying and borrowing ingenuity from nature. Scientific discovery tools, from pipettes to chromatography, were necessary to enable this process. I think of brain emulation models as the scientific discovery tool for studying the computational solutions nature has arrived at, so that we might deploy them elsewhere. Accurate brain emulation models also suggest that one could run at least some experiments digitally before performing them in vivo, saving valuable resources in contexts such as mental health research. And, most importantly, as we don’t yet understand the relationship between the firing of neurons, personality, and consciousness, perhaps brain models could help draw these links and rapidly test hypotheses. By building brains in silico, we will come to understand neuroscience. (Or, to quote Richard Feynman, “What I cannot create, I do not understand.”)

Of course, there are other ways of studying disease and consciousness that don’t involve replicating a complete brain on a computer. But the unique advantage of brain emulation models, I’d argue, is that they combine the manipulability of computational models with the biological realism of actual neural systems: a sweet spot that neither traditional neuroscience nor pure AI simulation can occupy.

Achieving brain emulation at human-scale during our lifetime is a monumental task. Success depends on both continued technological breakthroughs and a concerted effort to industrialize the whole pipeline of neuroscience. If this work weren’t already technically difficult, it’s also siloed across decentralized academic labs and is only being worked on by a few hundred researchers globally.

This essay is my attempt to describe what it will take to build a computer emulation of a full, human brain. Its details and estimates are distilled from over 3,500 hours of cumulative research with my colleagues, longer documents I’ve written on the subject, and discussions with more than 50 researchers.

Emulating a human brain will require three core capabilities: first, recording brain activity, second, reconstructing brain wiring, and third, digitally modelling brains with these data. Technology has matured to such an extent that the first brain emulation models for simple organisms like fruit flies or fish larvae could arrive within years. The same technologies could then be scaled to mice and humans, but emulations at that scale will require an enormous investment.

The Current State of Brain Emulation

Emulators are not the same as simulators.

Modern large language models can finish a sentence as a human would (and, increasingly, replicate other aspects of human behavior and affect, such as voices). Even so, these models are not brain simulators because they use different architectures from those used by the human brain as it processes information.1 This is similar to how airplanes achieve flight using jet engines and a metal frame, rather than by replicating the wings, feathers, and muscles of birds.

The brain models made in neuroscience, by contrast, are computer programs that emulate the underlying architecture with as much physical detail as possible. These models seek to instantiate the same neural wiring, firing rates, and overall processing structure of the real, flesh-and-blood neural networks that give rise to behavior.

There is no official list of brain components that must be modeled to create a brain emulation, but I’d argue that any viable one must include: a wiring diagram of the connections between neurons; modeling of certain non-neuron cell types and modulatory systems like hormones; accurate modeling of neural activity based on those factors; and changes in the neural wiring due to activity, also called neuroplasticity.

This list of components doesn’t seem intractable, yet no extant brain emulation model contains all of them. And this shortcoming is not for lack of trying. Scientists have developed basic brain models encompassing all the neurons in worms, larval zebrafish, and fruit flies. For mice, whose brains have approximately 70 million neurons (~500x more than fruit flies), we have only models of brain regions, such as 50 thousand neurons of a column in the visual cortex.

Scaling these “small” computational models to an entire human brain is, undoubtedly, computationally demanding. The human brain has about 86 billion neurons. The closest thing to a “true human brain model” created thus far is an effort, from 2024, in which researchers at Fudan University in China simulated all 86 billion neurons using a 14,000-GPU supercomputer. Their model ran at 1/120th speed for about five minutes of biological time.2

Even this most advanced effort is “basic,” however, because the scientists made several complexity-reducing assumptions in order to run the model at all. For example, they made educated guesses about the connectivity between neurons; indeed, the entire simulation’s neuronal wiring diagram was extrapolated based on data from an MRI scan of the author’s own brain, collected at a resolution one million times coarser than the width of a single cell. Even with access to a supercomputer, the researchers also had to downscale the total number of synapses per neuron to an average of 600, roughly five- to ten times less than reality.

To understand why it is so difficult to fully capture the complexity of a brain, consider the fruit fly. Even with their small brains, fruit flies behave in surprisingly complex ways. They walk and fly with rapid maneuvers, groom themselves, and engage in complex courtship rituals involving species-specific songs (yes, fruit flies sing!). They also learn, remember, and even possess idiosyncratic “personalities.”

In 2024, a group at UC Berkeley published a brain model capable of replicating aspects of a fruit fly’s brain as it processed sugar and fed. The model incorporated the exact wiring diagram of all 140,000 neurons in the fruit fly brain, which other scientists had meticulously digitized over a five-year span. To run the model, researchers fed simulated sugar signals into digital taste neurons and let neural activity propagate through the connectome. Each digital neuron computed its firing rate based on its inputs, connection strengths, and whether those connections were excitatory or inhibitory. The resulting activity patterns matched recordings from real flies to a reasonable degree, where firing rates and rhythms were in line with what scientists observe in real flies. And the model successfully emulated a single act of feeding and grooming, which was then validated against real flies’ brain activity.

Although impressive, this model is still far from a complete, virtual fly. Most of the virtual brain was silenced, so as not to interfere with the feeding response, and there was no flying, socializing, learning, or singing.

To revisit the flight metaphor, then, we are currently approaching the stage where we can model a bird’s basic wing flapping, but only under constant wind conditions, without obstacles or transitions into other wing positions — a useful starting point, to be sure, but still massively reductive. Scaling up this work to a full emulation, spanning the entire fruit fly brain, will require drastic improvements in three things: computational neuroscience, neural activity data, and neural wiring data.

Computational neuroscience provides the scaffolding for computers to represent neurons and brains, essentially the software and mathematical equations that describe the rules by which neurons process inputs and generate outputs. These equations include adjustable parameters (how fast a neuron recovers after firing, how strong a given synapse is, etc.), but the values of these parameters need data to be correctly set. That’s where neural activity and wiring data come in.

By recording what neurons actually do in living brains — when they fire, how fast, and in response to what stimuli — scientists can tune those mathematical parameters to match reality. This data must be collected from living organisms, using implanted electrodes that detect electrical signals or optical techniques that make active neurons glow under a microscope.

Finally, neural wiring data reveals whether neurons are connected to each other and, if so, to what degree. Unlike activity recordings, wiring data is obtained from dead tissue: researchers slice brain samples into ultra-thin sections, image each slice with electron microscopes, and then computationally reconstruct the three-dimensional structure of every neuron and synapse.

Building a brain emulation model requires each of these things, at a minimum.

Computational Neuroscience

Brain emulation models are most easily envisioned as large, interconnected networks of much smaller “digital neuron models” that talk to each other. A digital neuron, in turn, is akin to a mathematical formula, describing how a neuron behaves given certain inputs. As these formulas compound to include more and more neurons, the brain emulation model becomes a long, interconnected daisy-chain of functions that feed into each other.

The formula describing a digital neuron could be simple, capturing solely its “on” and “off” patterns, or it could capture everything from their ion channels to their membrane properties. In general, the more parameters these formulas contain, the more expressive they can be in recapitulating a neuron’s firing speeds, delays, recovery periods, and synapses. Even a single digital neuron with a few synapses has at least hundreds of parameters. In more detailed models, there are often millions. A complete brain emulation model consists of hundreds of thousands to billions, quickly driving the total parameter count for larger brains to levels that dwarf even today’s largest AI models.3

Each parameter also has its own storage and compute needs. Even with fairly simple neuron models, these computational demands accumulate quickly. In practice, an “uncomplicated” neuron with 100 to 10,000 parameters ranges between one to 100 KB in memory and one to ten million operations per second. This is roughly equivalent to the resource demands of dragging along a small 64×64-pixel emoji on a PowerPoint slide with a mouse. And again, this is per neuron. A single computer chip from the 1980s could run about 2,000 such simple, digital neurons.

Scaling this up 150,000 times, to capture all the neurons in a fruit fly, is possible with today’s consumer gaming hardware. But for a human-scale brain model, with its 86 billion neurons, running such a simulation would probably require all the compute contained in a large datacenter.

Although this seems daunting, brain emulation models are not bottlenecked by the computing speed of hardware. Today, the main computational bottleneck is “memory walls;” reading and writing the data quickly enough, rather than doing the computations themselves. Running a mouse brain simulation today, where each neuron is represented as the simplest possible entity, would demand about 20 GPUs. A human simulation would require 20,000 GPUs and still face the aforementioned slowdown issues due to GPUs spending most of their time moving data around.4

Why, then, are there still no “great” computational models of small organisms, like the worm or the fruitfly, if 1980s’ hardware was sufficient to run neuron simulations? The simple answer is that the central challenge of brain emulation is not to store or compute the neurons and parameters, but to acquire the data necessary for setting neuron parameters correctly in the first place.

Adjusting parameters to fit experimental data is called “model fitting.” The individual values in the mathematical equations are adjusted in such a way that the output of digital neurons resembles that of neurons observed in physical wet-lab experiments. For neural connections, the number and type of connections are ideally informed by anatomical scans that resolve neurons down to their smallest structures. But such data is limited due to the complexity and costs of experiments.

This is one of the main reasons why we continue to struggle to accurately replicate even small brains on computers. As with modern large-language models, which had to ingest the whole internet to become useful, brain emulation models will require significantly more biological data, spanning the full breadth of neural behavior, including neural activity and wiring data.

Neural Activity Data

One of the best ways to fit neuron parameters is to measure the precise firing patterns of every single neuron in the brain.5 But, alas, there are currently no methods available to do this at large scales.

Every existing method for scanning the brain must contend with various tradeoffs in resolution, volume of the brain covered, recording duration, sampling rate, and movements of the organism itself. No experiment to date has recorded the single-neuron firing patterns of an adult organism’s entire brain. In fact, the record for such an experiment is a mere 50 percent of neurons in the worm, C. elegans, and only for a few minutes!

Just imagine how difficult it would be to learn anything from a book if you only get a single random page (short duration instead of whole day), only the first part of each sentence on the page (incomplete coverage instead of whole brain), and additionally, some words in those fragments are missing (insufficient sampling rate instead of meeting maximum neuron firing rates). While this is obviously just a metaphor, it captures the current reality for neuroscientists.

That said, neural recording capabilities are rapidly improving, and two primary recording modalities exist that could capture the activity of individual neurons with sufficient resolution for training accurate models. Both approaches are still quite limited, however, in the number of neurons they can record and in the invasiveness required.

The first is microelectrode arrays, or MEAs, which are small, implanted chips able to record electrical signals directly from tissue: usually up to 1,000 neurons at a time.6 They are akin to dangling many microphones over a conference room to pick up sounds from individual speakers. MEAs, though, don’t easily scale across large brain volumes, as the needle threads containing each electrode must penetrate (and thus damage) brain tissue. With MEAs, it’s also difficult to figure out which neurons produced which signal.

The second option is to employ optical microscopy to watch neural activity directly. For example, scientists can genetically engineer neurons to express a fluorescent protein, called a calcium sensor, which emits photons when active. Microscopes and lasers are used to “read out” or video record the firing of each neuron containing these sensors.

This approach, like the first, is limited to only small, microscopic segments of the brain; an area a few millimeters wide, or up to one million neurons in total. And much like MEAs, optical single-cell recording can carry surgical risks, as scientists must physically dig into brain tissue to watch the neurons inside. This method can also restrict the natural movements of an organism; in mice, for example, a motion-sensitive microscope must be mounted on their heads.

But still, progress in neural recording technologies has been swift. In the 1980s, electrodes were capable of sampling perhaps five cells in total, about 200 times per second (~ 10³ data points per second). Today, with optical imaging, researchers can instead record one million cells about 20 times per second (10⁶). The whole-brain data rate needed for mice, however, would be 14 billion (10⁹), while humans would require 17.2 trillion (10¹²) per second.7 So while we have increased data rates by 1,000x over the past 40 years, we have far to go before we can accurately sample mammalian brains.

Finally, just because it’s possible to record one million of the 70 million total neurons in mice, or record 1,000 neurons at a rate of 200 times per second in larval zebrafish, does not mean it’s possible to record all 300 neurons in a single C. elegans worm. In fact, the best recordings to date capture about half the neurons in immobilized worms, and less than a third when the worm is allowed to move freely.

The main obstacle is the worm’s motion; while crawling, its 50-micrometer head swings nearly twice its own diameter per second, and the body can twist into sinusoidal, circular, and omega shapes that no current algorithm can follow. I’m making this point in detail because the lack of a working worm brain emulation model is a common objection lobbed about by brain emulation critics, but even the smallest organisms can present data collection difficulties, sometimes greater than those of larger organisms with many more neurons.

Techniques do not easily transfer across species: first, because an organism might lack a genetic toolkit to express fluorescent sensors; second, because they can’t tolerate the fixation required to hold still under a microscope, and third, because their neurons sit too deep for optical imaging to reach. Resolution requirements also differ as fruit fly neurons are much finer than mouse neurons, demanding more precise imaging. In practice, each organism often requires its own methodological breakthroughs.

In contrast to neural activity data, neural wiring data acquisition fortunately has a more generalizable path forward. There, the fundamental pipeline — slicing, imaging, and reconstructing — generally works well across species. The challenges are formidable, but primarily ones of scale, cost, and labor.

Neural Wiring Data

A single neuron often extends its tendrils to touch thousands of others in a labyrinthine network. Wiring diagrams of these vast networks, called “connectomes,” are critical for understanding how neural circuits actually compute.

Broadly speaking, building a brain connectome demands four phases of work. First, researchers slice brain tissue into ultra-thin layers. Second, they image each with electron microscopes. Third, they use computer algorithms to stitch each image together into a detailed, 3D model, much like building a puzzle with millions of microscopic pieces. Finally, humans perform quality control on the output of the algorithms.

To reconstruct the connections between each neuron, images must have a high enough resolution to differentiate between even the smallest parts of a cell. Each pixel, in each image, represents about 10 x 10 x 10 nm³ of brain volume.8 After capturing millions of images, human proofreaders manually scroll through each one to spot split-and-merge errors from the neuron tracing algorithms. These errors occur when algorithms either fragment a single neuron into multiple pieces (split) or incorrectly combine distinct neurons into one (merge). Proofreading is by far the least scalable and most labor-intensive process in generating a connectome. For example, it takes 20 to 30 minutes to proofread a single image of a fruit fly neuron, but it can take 40 hours or more to proofread a substantially bigger mouse neuron with its more complex and multitudinous branches.

Since the first connectome of the worm C. elegans was published in 1986, nine additional worms and two fruit flies have had their wiring diagrams completely reconstructed. Meaningful amounts of brain tissue — such as regions of the spine in smaller organisms, or millimeter-scale volumes of larger brains — have also been imaged for ten additional organisms, but these data have not yet been proofread and thus are generally not usable for computational brain modeling.

Fortunately, the total costs for reconstructing neuron wiring diagrams have fallen substantially over the last few decades. The average cost to reconstruct each neuron in the first worm connectome, published in the 1980s, was about $16,500. Recent projects now have a per-neuron processing cost of about $100 for small organisms, such as fruit flies. For rodents, with their more complex neurons, the price for proofreading alone is about $1,000 per neuron. To reconstruct a whole brain connectome, at an estimated cost of one billion dollars, these end-to-end prices must fall to $10 per neuron for the mouse and $0.01 per neuron for humans.

These falling costs apply to wiring data alone and are considerably higher for the “gold standard” data for brain emulation: datasets that merge neural wiring with activity recordings from the same individual organism. Such aligned datasets are much more labor-intensive to produce, but essential for building models that accurately capture both structure and function.

Researchers from Harvard, Janelia, and Google Research have been collaborating over the past five years to scale this approach of combined neural wiring data collection and neural activity recording from the same individual organism to build an aligned, whole-brain dataset. After hundreds of trial-and-error attempts, these researchers have recorded 70,000 neurons from one larval zebrafish during behavioral tasks and consecutively scanned the same organism’s brain tissue using an electron microscope. Neuron reconstruction, specifically the proofreading, was the most laborious part of this project and is still ongoing. However, the authors published the “Zebrafish Activity Prediction Benchmark” (ZAPBench) March of 2025 and expect the full connectome to be ready in 2026.9

Taken together, the tooling across computational neuroscience, neural recording, and neural wiring data has improved radically over the past decades. While capturing the full complexity of mammalian brains cannot be understated, the path to the first brain emulation models is now visible. And even if the journey is long, conquering each of the milestones along the way will be remarkable in its own right.

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The Roadmap for Brain Emulation Models

I believe that to get to human brains, we first need to demonstrate mastery at the sub-million-neuron-brain level: most likely in zebrafish. For such organisms, like the fruit fly, a well-validated and accurate brain emulation model could be created in the next three to eight years. This claim is based on dozens of conversations with experts, as well as guesses informed by technological trendlines.

Achieving this goal will depend primarily on more and better data to fit parameters, which in turn is bottlenecked by funding and the achievement of some key technological breakthroughs. But there have been a couple of recent advances that will soon make this feasible: algorithms that eliminate human proofreading and methods to record neural activity over wider swaths of the brain. At the scale of insect-sized organisms, we are nearly capable of overcoming such bottlenecks.

Google Research recently released PATHFINDER, for example, a machine-learning-based neuron tracing tool that reduces human proofreading by about 80x. The key innovation is a neural network trained on thousands of human-verified neuron reconstructions, learning what real neurons look like: their branching patterns, curvatures, and proportions. When the system proposes merging two fragments, the model scores whether the result looks biologically plausible, automatically rejecting the kinds of errors that previously required human review.

This neuron tracing tool will undoubtedly be useful for ongoing, large-scale brain scanning projects. In 2023, the National Institutes of Health launched the BRAINS CONNECT project, which aims to scan about 1/30th of a mouse brain by 2028 and build infrastructure for a complete mouse neuron wiring diagram by 2033. The 2023 Report by the Wellcome Trust, mentioned in the introduction, concluded the main expenditure for such a project would be human proofreading, but algorithms like PATHFINDER may substantially reduce those estimates.

Another major boost to mapping connectomes is a technique called “expansion microscopy.” First reported in 2015, expansion microscopy iteratively expands tissue using polymers similar to the absorptive material found in diapers. In other words, rather than zooming into tissues using microscopes, this technique enables researchers to physically blow those tissues up, thus increasing resolution. The technology has gotten so good in recent years that scientists can now expand nanometer-sized structures, like synapses, to volumes large enough for standard light microscopes to take pictures and trace neurons; no more electron microscopes required.10

Expansion microscopy also addresses another key limitation of electron microscopes: namely, that they produce only grayscale images. While scientists can see cells clearly, they can’t easily tell what kind of neuron they’re looking at. Expanded tissue, by contrast, can be washed with fluorescent dyes that light up specific proteins of interest: membrane receptors, neurotransmitters, and other molecular markers that reveal how different neurons actually function.

The focused research organization E11 Bio is leveraging this molecular labeling capability to tackle the proofreading challenge. Rather than training algorithms to trace neurons more accurately through grayscale images as PATHFINDER does, E11 seeks to make neurons easier to distinguish in the first place. By tagging each neuron with a unique combination of protein “barcodes,” they give every cell its own color-coded ID. This would make it far easier for algorithms to trace neurons across thousands of images. E11 hopes this approach will make whole mouse connectomes feasible in the coming years.

Regardless of the approach, assuming proofreading will be basically automated in the upcoming years, additional small organism connectomes such as fruit flies would be in the low hundreds of thousands of dollars; a first mouse connectome in the low hundreds of millions, and a marginal one in the tens of millions of dollars. For human-scale brains, a simple extrapolation would yield 1,000x more: about a hundred billion for the first and tens of billions for consecutive ones.11

Many experts in the field share the conviction that we are on track to “solving” proofreading in the near term. Whole-brain, single-cell recordings, on the other hand, especially at the mammalian brain scale, will remain infeasible in the same time period. For any organism with a brain bigger than a cubic millimeter, we need to find innovative ways to compensate for the lack of comprehensive single-neuron recording coverage in our computational models.

For larger brains, we will likely increasingly rely on methods that can infer neural activity from structural and molecular data alone (which we can acquire in deceased brains at bigger and bigger scales). This approach remains speculative and, given how much promise it holds, surprisingly underexplored. Iteratively larger studies, probably in the tens of millions of dollars, could help determine the exact scale and type of data eventually required for mammalian-scale projects.

The vision of a digital, sub-million-neuron brain emulation model, however, also hinges upon a considerable investment, probably on the order of $100 million. With this amount, projects could funnel somewhat piecemeal research into an industrialized pipeline for recording and scanning state-of-the-art whole-brain datasets from multiple adult insect or developing fish brains. The aforementioned aligned zebrafish datasets have cost more than $10 million since inception in 2019, but subsequent ones should be much cheaper. Ideally, it would even be possible to rely on many replications and variations of such datasets, combining them with molecular annotation and other bespoke data acquisition techniques. This way, we can answer the question of what makes brain emulations better empirically, rather than relying on expert opinions. Also, it would provide space for investigations into neuroplasticity, as well as non-neuronal cell types and modulatory systems, all of which are likely core components of brain emulation models. Ultimately, models built upon such datasets would set a ceiling on today’s emulation abilities and, importantly, clarify the data needs for larger brains.

If I had to put a number on optimistic budgets and timelines for human brain emulation today, I would hazard: Conditional on success with a sub-million-neuron brain emulation model, a reasonable order of magnitude estimate for the initial costs of the first convincing mouse brain emulation model is about one billion dollars in the 2030s and, eventually, tens of billions for the first human brain emulation model by the late 2040s. My error bars on this projection are high, easily 10x the costs and ten additional years for the mouse, 20 to 50 years for humans.

Readers familiar with recent AI progress might wonder whether these timelines are too conservative. AI will provide extraordinary acceleration in some places, but I’m skeptical these gains will multiply across a pipeline with dozens of sequential dependencies and failure modes. Brain emulation is fundamentally not a digital process; Core bottlenecks involve physical manipulation of biological tissue, with time requirements dictated by chemistry and physics rather than compute power. The field requires deep integration across disciplines and tacit knowledge accumulated through years or decades of hands-on training. Capital costs of specialized equipment and ethical considerations around human brain tissue add to these constraints. Scientists might also make new observations tomorrow that complicate the picture further, such as realizing that not just a few, but hundreds of distinct molecular annotations might be necessary to accurately model a neuron’s activity.

Finally, it’s important to highlight that neither the sub-million-neuron organism nor the human estimates are considering brain models of a specific individual with all their memories and personality traits. Given that we will almost certainly aggregate data from many organisms to get sufficient data coverage, I expect the first brain emulation models to be generic, rather than personality-preserving. The feasibility of flawless transfers of a whole identity and its continuity onto a computer, as portrayed in science fiction, remains yet another step up the speculation ladder.

Despite these uncertainties, it seems we are the first generation of humans crossing the strangest threshold of all: from biology to technology, from evolution’s creation to our own. This refers not only to AIs simulating our behavior, but also to computer programs eventually emulating the very architecture of our brains. Before we can achieve this, there is a mountain of technical work and innovation to be done. The same holds for discussions surrounding the philosophy, ethics, and risks of brain emulation, which fall outside the scope of my investigations. Even so, what seemed absurd to me in 2023 now appears possible.

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To learn more about brain emulation, see our full report.

Maximilian Schons, MD, is the project lead for The State of Brain Emulation Report 2025. His research consultancy focuses on responsible innovation at the intersection of biotech and AI. He has held senior positions in German medical research consortia and served as Chief Medical Officer for life-science startups. More at mxschons.com

Cite: Schons, M. “Building Brains on a Computer.” Asimov Press (2026). DOI: 10.62211/92ye-82wp

Acknowledgements: Niccolò Zanichelli, Isaak Freeman, Anton Arkhipov, Philip Shiu, Adam Glaser, Adam Marblestone, Anders Sandberg, Andrew Payne, Andy McKenzie, Anshul Kashyap, Camille Mitchell, Christian Larson, Claire Wang, Connor Flexman, Daniel Leible, Davi Bock, Davy Deng, Ed Boyden, Florian Engert, Glenn Clayton, James Lin, Jianfeng Feng, Jordan Matelsky, Ken Hayworth, Kevin Esvelt, Konrad Kording, Lei Ma, Logan Trasher Collins, Michael Andregg, Michael Skuhersky, Michał Januszewski, Nicolas Patzlaff, Niko McCarty, Oliver Evans, Ons M’Saad, Patrick Mineault, Quilee Simeon, Richie Kohman, Srinivas Turaga, Tomaso Poggio, Viren Jain, Yangning Lu, Zeguan Wang, Xander Balwit, Robert Bölkow, Dion Tan, Felix Schons, Sarah Gebauer, Richie Kohman, Red Bermejo, Grigory, Ethan, Florian Jehn, Philip Trippenbach, Devon Balwit

… and to all the scientists and lab animals the research is based on. Any errors, oversimplifications, or misinterpretations are entirely mine. Illustrations and animations by Iris Fung.

Further reading

• 2008 Whole Brain Emulation Roadmap,

• 2021 NIH Brain Connectivity Workshop Series,

• 2023 Wellcome Trust Report Scaling up Connectomics, and

• our 2025 full-length State of Brain Emulation Report 2025

Please send questions and comments to brains@mxschons.com.

By Brady Huggett

Most of the people in this story have already died, but there are still some who remember a finding that captivated the developmental biology field decades ago. The story concerns a molecule, known as the “head activator,” which was believed at that time to be a short neuropeptide necessary for head regeneration in the freshwater cnidarian hydra.

In 1973, a German graduate student named H. “Chica” Schaller published a paper under the prolix title: “Isolation and characterization of a low-molecular-weight substance activating head and bud formation in hydra.” The work was conducted in the Alfred Gierer lab at the Max-Planck-Institute for Virus Research in Tübingen, Germany. The lab had been working to understand morphogenesis (the process by which an organism develops) in Hydra attenuata. In the course of this work, they uncovered a substance that they claimed was responsible for initiating head formation in hydra.

Chica’s paper emerged as the fields of developmental biology and molecular biology were intersecting. In 1924, Hans Spemann and Hilde Mangold demonstrated the concept of an “organizer”— a cluster of cells within the newt embryo that could induce or guide the development of surrounding tissue when inserted in another species of newt. In the elapsing decades, the field had observed similar organizational activity across species, but the molecular underpinnings for these phenomena were unknown. Chica’s 1973 paper drew on these findings to propose a similar mechanism in hydra, putting her name on the developmental biology map.

Later, she and her colleague Hans Bodemüller would sequence the substance — the first morphogen ever sequenced, actually — and make it available to any interested researcher. The head activator became synonymous with Chica’s name. Over the years that followed, both she and her colleagues published a string of papers about it, as well as studies on inhibitors in hydra, and Chica was asked to present at conferences in both Europe and the U.S.

The problem was that her findings were seemingly impossible to replicate. Both her early colleagues and the people in the larger Hydra field eventually abandoned them: Stefan Berking was unable to repeat her work; Charles David watched as new explanations for hydra morphogenesis arose; and Robert Steele decided her claims weren’t worth wasting funding dollars on.

Today, while the Hydra remains a useful model for the study of nerve nets, aging, and regenerative medicine, new explanations have emerged to explain morphogenesis in hydra. The mystery of Chica’s “head activator” has never been solved. The history of how it was discovered and eventually rejected illustrates how science progressed over her lifetime, moving from embryology to molecular biology to genetics.

But the real reason I spent months reading and translating books and calling around to locate interview subjects was to understand how this mystery affected the people involved; to learn why the one person who openly challenged Chica and the head activator, a German biologist named Werner Müller, bore the scars of that battle to his grave.

Beginnings

Hydra have a thin body column, generally shy of an inch, with a disk-like foot at one end and a mouth surrounded by tentacles at the other. The tentacles have stinging cells, and the animal eats by grabbing, paralyzing, and ingesting its prey, often small crustaceans. These cnidarians travel by somersaulting, head-over-foot, and they mostly reproduce by asexual budding. But because they possess a high proportion of stem cells, their bodies constantly renew and large portions can regenerate. For this reason, they are sometimes referred to as immortal.

The hydra is thought to have first been identified by Antoni van Leeuwenhoek, who observed it with his microscope. The naturalist Abraham Trembley, however, made it famous. Trembley came across the animal in 1739, a cylindrical thing attached to the stem of an aquatic plant he pulled from a ditch. He put the plant in a jar of water and watched the polyp reach upward with its thin arms. When he shook the jar, the creature contracted sharply, as if startled.

At first, Trembley thought the hydra was a plant, but when he cleaved it in two, severing the “foot” from the “head,” and witnessed both halves producing fully formed animals, something prickled in his brain. The more he observed “the two parts in which the reproduction” took place, he wrote, “the more their activity called to mind the image of an animal.”

Trembley set about examining the hydra in nearly every way possible: slicing it in half, attempting to turn one inside out, and removing its tentacles, chronicling these experiments exhaustively in his Mémoires.

Chica encountered the animal more than 250 years later. Born in 1937 in Alzney, Germany, her birth name was Hildegard Kornmayer. Her father died in World War II, and Chica sometimes thought of herself as a half-orphan. Her mother married again and ran the textiles business in her new husband’s successful department store.

Chica’s grades in high school were middling. But she had artistic leanings, writing poems and taking photographs, and she cultivated an independent streak — sometimes wearing tight, three-quarter-length pants, for instance, which was rare for women at the time.

After graduation, Chica attended the Heidelberg Dolmetscher-Institut, a language school, where she studied Spanish and English. She traveled to Spain in the summer of 1958 with a fellow linguist named AnnMarie, a tall, striking red-head. Chica was somewhat deferential to AnnMarie and gave her the nickname “Mammi.” In return, AnnMarie gave Hildegard the nickname “Chica,” a name she carried into her scientific life.

While playing tennis in Spain, AnneMarie met a German chemistry student from Heidelberg named Klaus, who sometimes brought along his friend Heinz Schaller, also a chemistry doctoral student. After they returned to Heidelberg, they stayed in touch. Chica and Schaller fell in love and married about two years later, before going to the University of Wisconsin at Madison for Schaller’s post-doctoral work.

Chica wasn’t happy abroad. She didn’t like Madison’s climate or people and was bored with the translating and secretarial work she was able to find. While she enjoyed the exploratory trips she and Schaller took through the country and Canada, she was happy to return to Germany in January 1963 when Schaller took a research associate position at the Max Planck Institute for Virus Research in Tübingen.

Chica, then 26, decided she needed more education and enrolled in a biology undergrad course with a focus on genetics and biochemistry. She graduated in five semesters and went directly into a PhD program in the winter of 1966-67, joining her husband at Max Planck, where she became Alfred Gierer’s graduate student.

Gierer had already been nominated for the Nobel Prize in Chemistry twice by this time, but he had become fascinated by the generation of spatial patterns — how tissues and cells become arranged — in developmental biology. His lab wasn’t quite sure how to study this, however, until an assistant professor in the zoology department, named Werner Müller, suggested they use the Hydra.

By the late 1960s, Gierer, the American postdocs Hans Bode and Charles David, and the German graduate students Stefan Berking, Ekkehard Trenkner, and Chica Schaller, were investigating the Hydra in earnest. They were joined by physicist Hans Meindhart, who wanted to explore biological questions via computer modeling. Gierer suggested they develop a theory for how hydra formed.

In 1972, the lab showed that the polarity of the morphogenesis in hydra came not from cellular orientation — where the cells were located in the animal — but from some other guiding principle. David recounted how the group could all but decimate a hydra, pushing the animal through a fine mesh, and from this “completely random mass of cells — let’s say 100,000 cells,” two polyps would form. “It takes four or five days to have this happen,” David told me, “but you’re creating order out of complete chaos.”

Later that year, Gierer and Meinhardt published the fundamental paper on this idea, entitled “A theory of biological pattern formation.” It established what would be called the Gierer-Meinhardt model, which explained, among other things, the way organized tissue arose from a mass of cells. This model, which built off earlier work by Alan Turing, showed that spatial order can emerge through interacting “morphogens”: an activator that promotes both its own production and that of an inhibitor, which diffuses more widely and suppresses the activator. This interplay of short-range activation and long-range inhibition, the paper asserted, could spontaneously generate organization, even without preexisting structure.

“For the first time,” David said, the paper “provided a very clear mechanism” for how activating and inhibiting substances along a gradient in the body of hydra could cause regeneration.

But no one knew what substances accounted for this, and Gierer asked Chica, his graduate student, to investigate. Chica began by reading the literature, including Lesh and Burnett, and Thomas L. Lentz, who published The Cell Biology of Hydra. She also read work by Müller, who had been searching for a substance that could cause regeneration in the cnidarian Hydractinia, and had made a similar attempt to “isolate and accumulate the ‘polarizing inducer’” in hydra. These researchers had all presented evidence that an unknown substance “is present in crude extracts of hydra that may determine head formation,” as Chica wrote in her 1973 thesis.

After years of work, Chica claimed to have found the “head activator” molecule; one of the four ingredients responsible for Hydra’s regenerative abilities. She had taken 30,000 hydra and used ultrasound to break open their cells, creating a crude extract that she spun down in a centrifuge. From this, she was able to isolate and enrich a substance of a low molecular weight that was susceptible to degradation by enzymes, suggesting it was likely a peptide.

Next, she set about testing the activity of the substance. She began with hydra that had been starved for 24 hours and showed no signs of growing a new head. Then she cut away the top of the animal, including its mouth and tentacles, and incubated the body stem for six hours in either regular hydra growth medium, or the same liquid with her isolated “head activator” substance added in. After those six hours, both groups of hydra were placed in regular growth medium and, after 48 hours, Chica counted and compared new tentacle growth between the two groups. The results showed, she wrote, that “in its purified form the substance not only stimulates the number of tentacles in regenerating animals and the rate of head regeneration, but also the number of buds and the rate of bud formation.”

Taken at face value, this experiment seemed to suggest that Chica had isolated one of the molecules behind head growth in hydra. The theory of morphogenesis had its first morphogen.

A Big Splash

Chica’s paper vaulted her to the top of the developmental biology world. She was asked to speak at conferences, both locally and in the United States. But the Gierer lab was young; its members needed to advance in their careers, and it split up around 1974. Bode eventually would move to a professorship at UC-Irvine. Berking continued studying morphogenesis in the Gierer lab, Trenkner moved to a postdoc in New York City, and David also went to New York, to Albert Einstein Medical School as an assistant professor.

Tension between Chica and Müller had already surfaced in Tübingen. Chica was “quite smart,” David told me, but she could have “a very loose tongue.” And she “took a dislike to Werner Müller, because he was absolutely the opposite. He was a staid, old-fashioned German professor: God is in heaven, and two-plus-two equals four, and evolution happened, and that’s it.” David also found Müller to be very intelligent, but “he was so utterly different from Chica that this animosity developed very early on.”

It didn’t help that the Gierer lab had been a fun, tight unit. Its members sometimes “went skiing together, had dinner together three times a week,” David said. And it was coming at developmental biology from fresh angles: Gierer, the physicist; Meinhardt, the theorist; David, the biophysicist; Bode, the molecular biologist; and Chica, the former linguist. Müller, on the other hand, was a classically trained biologist, doing science in what might have felt to them like the stodgy old way.

“We were in a completely different world, and it was pretty easy for us to develop a certain degree of contempt for Werner Müller as being kind of old-fashioned, slow-witted,” David told me. “None of this was actually true, but this image kind of developed.”

By the time the lab broke up, Schaller — Chica’s husband — had become a full professor and the head of the Institute of Microbiology at Heidelberg University. Chica, having finished her doctorate, took a position as group leader at the European Molecular Biology Laboratories in Heidelberg to remain close to him.

She continued to work with hydra, but the position at EMBL was only a five-year appointment, and by 1979, Chica again needed to find a new posting. Müller, meanwhile, had moved from his assistant professor position at the University of Tübingen to professor at the Technical University of Braunschweig, and then to full professor and Director of the Zoological Institute at the University of Heidelberg. Though Chica did not seem to admire him, he had space and welcomed her, possibly hoping her background in molecular biology would bring a fresh perspective to his department. She funded her work with grants.

Then, in 1981, Chica, working with the biochemist Heinz Bodenmüller, revealed the actual sequence for the peptide she had claimed was the head activator. It was produced by nerve cells, they wrote, stored in neurosecretory granules, and had the amino acid sequence of pGlu-Pro-Pro-Gly-Gly-Ser-Lys-Val-Ile-Leu-Phe.

The sequenced compound brought the head activator out of theory and into the physical world. Chica and Bodenmüller filed a patent on the head activator substance in Germany even before publishing their paper, following that with an application at the U.S. patent office. The compound, they claimed, was of interest as “a research substance and pharmaceutical composition,” and Chica had the Swiss company Bachem synthesize it, making it available for anyone to buy and experiment with.

Meanwhile, the parts of the Gierer-Meinhardt model were falling into place. Because Chica had sequenced the head activator, it seemed possible the other three substances — head inhibitor, foot activator, and inhibitor — would eventually be identified as well. That left proving that these substances existed in gradients along the hydra body, evidence for which was soon supplied by Harry MacWilliams, a Harvard University researcher.

MacWilliams focused on foot growth in hydra, and the Gierer lab in 1972 had invited him to visit. When he returned as a postdoc fellow, he used a grafting technique1 to show that foot and head activation acted on a gradient — meaning that activation for a head was “confined to the presumptive head zone” and something similar happened in the foot region with foot growth. This, MacWilliams wrote, was “consistent with a version of the Gierer-Meinhardt model.”

MacWilliams published two papers in 1983 detailing this work. Though other hydra morphogens had not yet been sequenced, the hydra community then had the head activator and the “Gierer-Meinhardt model, and … Harry MacWilliams’s grafting experiments,” Steele told me. “Those three things in aggregate cemented what seemed like a consistent story.”2

Does It Replicate?

Cracks began to emerge almost immediately, however, as other researchers struggled to replicate Chica’s findings.

Part of the difficulty might have been due to the demands of her initial experiment, which involved meticulously harvesting, grinding, and then centrifuging vast amounts of hydra. “It was very hard work,” David told me. “It’s amazing that she was able to get enough to generate a sequence, and then show that the synthetic head activator actually functions.”

The small quantities of hydra such work yielded were indeed an issue, which Chica got around by seeking out another raw material source. In their 1981 paper, Chica and Bodenmüller wrote that they isolated the head activator from the sea anemone Anthopleura elegantissima, which is larger than hydra, abundant, and contained a substance that “seemed to be identical to the head activator from hydra.”3

Switching out hydra for sea anemone may look a little like a “bait and switch,” Steele said, but it was reasonable to say “if it’s in one cnidarian, it’s in another.”

Regardless of how (and from what organism) the compound was isolated, testing its activity wasn’t particularly easy, either. Chica stressed that everything had to be done exactly so — the animals needed to be healthy, for instance, and the cutting done quickly — or it wouldn’t work.

That left the door open for criticism, which started even before the head activator substance was sequenced. At UC-Irvine, which had an active hydra community, developmental biologist Dick Campbell and colleagues were able to strip a hydra of all its interstitial cells, leaving the animal without nerve or nerve stem cells — the same cells in which the head activator substance was apparently made and released from. But even in this state, the hydra still exhibited polarity reversal, and the animal was “capable of essentially normal development,” the authors wrote in a 1978 paper Observing this work, Jonathan Slack, from the Imperial Cancer Research Fund in London, noted in Nature that it “seems that the significance of the head activating substance will now have to be reassessed.”

Yet it does not seem that Chica did so. Decades later, she would suggest that neurosecretory granules must form in the epithelial cells, rather than interstitial cells, and therefore lead to the development of the head activator.

Her explanation did not work for Steele, who interacted with Campbell at UC-Irvine and told me that Campbell had “very convincingly” shown that “nerve-free hydra can bud and regenerate heads.” Steele did “not buy” Chica’s argument that epithelial cells leap into the breach and produce head activator in hydras without nerves. “There is no obvious biological logic for that,” he told me. “Why would epithelial cells be able to take over a function that evolution has not prepared them for?”

Others were likewise questioning what they thought they had learned about hydra. Berking, who had worked in Chica’s lab at EMBL to isolate head and foot inhibition substances in hydra, wrote in Roux's Archives of Developmental Biology in 1983 that these proposed substances were actually “an artefact” produced by the separation process. In fact, he wrote, substances could simply be found in Dowex 50 — a liquid used in chemistry analysis — that would also inhibit head regeneration. Berking added that “we have not been able to confirm that the extract from heads preferentially inhibits head regeneration and the extract from feet preferentially inhibits foot regeneration.”

Berking’s comments might have ended their friendship. She published a reply within the year:

In a recent publication in this journal, it was claimed that the head inhibitor we isolated from hydra is a Dowex artefact, that a separate foot inhibitor does not exist in hydra and that the only inhibitor that has so far been isolated from hydra is one which inhibits head and foot regeneration equally well. These statements are incorrect and require a response.

Chica wrote that she had repeated Berking’s experiment and did not see the Dowex artefact, concluding, “I do not see any solid argument for not maintaining our present position that several chemically different inhibitors can be isolated from hydra with different specificities for head or foot formation.”

Bad Blood

By 1984, Chica was once again seeking a full professorship. The hydra community in Germany was small and tight, a group of researchers siloed by geography, all studying the same animal. They sat on review committees for each other’s proposals, and they saw each other at conferences.

All of that might naturally have bred competition, but the tension that had been bubbling between Chica and Müller since their Tübingen days grew after she set up in Müller’s department. The two groups sometimes had co-lab meetings, said Monika Hassel, a student in Berking’s lab around this time, and during them Chica often made “derogatory and snippy comments” that were “hard to stand.”

To make matters worse, Müller never believed in the head activator. And David told me that since Müller was convinced that the head activator didn’t exist, he thought anybody who credited it was foolish.

Sometime around 1984, Chica and her co-author, the hydra researcher Sabine Hoffmeister, sent out a paper concerning a biochemical marker for foot differentiation in hydra. The journal, Roux’s Archives of Developmental Biology, sent the paper for review to Müller, given his experience as a hydra researcher. Müller had a problem with a figure showing the concentration of head and foot inhibitors in parts of the hydra. When Chica saw his comments, she asked to have him removed as a reviewer, then redid the experiment herself.4 She turned in the new results to the editor, who published the paper.

Meanwhile, Chica applied for professorship positions in Karlsruhe and Regensburg, but didn’t get them. She turned down an offer in Bochum and also in Braunschweig; what she really wanted was a position in Heidelberg, which would keep her close to her husband. In 1988, an offer was finally on the table for a professorship in ZMBH (Center for Molecular Biology) at the University of Heidelberg. David wrote her a strong letter of support, calling her “one of Heidelberg's most distinguished scientists.”

Yet Chica did not get the position. The reason, from what I can gather, was Müller, who once told Hassel that, in his hands, the head activator “never worked” as described in Chica's publications, and because of this felt it was “not appropriate” for Chica to “become a professor in Heidelberg.”

And at some point during Chica’s review process for the Heidelberg professorship, David told me, there was “an attempt by [Müller] to prove that she had falsified her data.”

This accusation caused an explosion. The University Senate was called in. The subsequent inquest was conducted in English, not German, Hassel said, because English is more broadly understood in the scientific community. This decision benefited Chica, who had studied English and lived in the U.S. Müller, however, struggled to communicate as clearly in English. While this may have swung the senate in Chica’s favor, the underlying accusation of falsified data likely proved more important. David said he was asked to serve as one of the external referees and discern whether Chica had done so, but Müller’s accusation “simply wasn’t true,” he said.

In the end, the University Senate found for Chica. Müller, Hassel told me, was fined 40,000 Deutschmarks (~$22,760) — a damaging sum. “He had a young family, and he didn't have any money in the bank,” she said. “So it was terrible.”

It had all become “extremely ugly,” David told me. Müller had been shamed and fined, but the mess had somewhat tarred Chica, too. In the end, David said, “Chica had no choice. She couldn’t stay in Heidelberg,” and in 1991, she took a full professor position at the Institute for Molecular Neurobiology in Hamburg instead.

Moving On

By the ‘90s, interest in the head activator was waning. “So many people tried to repeat Chica’s experiments,” Berking said. “It was frustrating. A few effects were there, and if you tried again, it was no more. People lost patience to study the head activator.”

Science marched onward, and in the years following, new discoveries undermined the head activator. In 1997, a group of researchers in Japan, working with David, Bode, and Thomas Bosch, isolated 286 peptides from Hydra vulgaris (called Hydra magnipapillata at the time), and tentatively determined the amino acid sequences of 95 of them — none of which were the head activator. Because the group did not identify all peptides in hydra, it was possible that the head activator still lurked somewhere in the animal, but its absence from the data further damaged the credibility of Chica’s peptide.

Then, in 2000, a group of researchers published a paper suggesting that the Wnt-signaling pathway was behind head regeneration in hydra. The pathway appears across species, and includes a network of proteins that control cell differentiation and tissue and organ formation in embryonic development. The pathway molecules Wnt and Tcf are expressed in the top of the hydra, near the mouth and tentacles, and the authors, led by Thomas Holstein, wrote that the hydra Wnt signaling pathway was involved in “local self-activation in the hydra head organizer.”

The work was enough to convince David that “the Wnt-signaling pathway is the activator” in the Gierer-Meinhardt model for hydra head morphogenesis, he told me. It dealt another blow to Chica’s head activator, though it was still possible that the peptide she had championed was a component upstream of the Wnt pathway in hydra.

Conclusive evidence against the head activator emerged in 2010, however, when the hydra genome was sequenced at the J. Craig Venter Institute. The work was done by Venter, Steele, Bode, David, and 70 other researchers from around the world. The genome came from Hydra magnipapillata, and the authors estimated that “the hydra genome contains ~20,000 bona fide protein-coding genes.” But the “head activator peptide sequence is not encoded as such in the hydra genome sequence,” the authors wrote, noting that “the origin of the Head Activator peptide remains unresolved.”

The sequenced hydra genome was “the final nail in the coffin” for Chica’s head activator, Steele said. The peptide simply wasn’t encoded in the hydra genome, so whatever Chica had been experimenting with could not have come from the animal itself.

By then, Chica had mostly moved on, too. After taking the professorship in Hamburg, she opened a new chapter in her life, focusing on G Protein-Coupled Receptors, which are found on the surface of cells and respond to extracellular signals. She and Schaller also shifted their focus to philanthropy. Schaller had been a founding member of the biotech company Biogen in 1978, and by the 1990s, his shares had turned him into a millionaire. He and Chica reportedly put three million euros into The Chica and Heinz Schaller Foundation, which has funded basic biomedical research since 2000 and given out prize money to Heidelberg-based young scientists since 2005.

Schaller died on April 10, 2010, at 78, after a “short period of severe illness.” Chica herself was in her 70s by then and seemed to grow wistful. She began working on a book about her personal and professional life with Schaller. She found herself revisiting hydra and the head activator.

In October 2015, Chica emailed Steele to ask about a “multiheaded mutant” from the Chlorohydra viridissima strain, which had been created in 1961. Chica had worked with the mutant in the ‘70s and wanted to know what genomic analysis might reveal about the mutant’s head formation. Chica seemed to be asking Steele if he’d do the sequencing, he told me, but Steele “had absolutely zero interest” in throwing any money or time at the head activator.

Chica also told Steele that the head activator sequence was derived from a substance also found in sea anemone and rat intestine.5 The rat genome had been sequenced in 2004, and Chica admitted that the head activator “sequence is not present.”

“Conclusion: we must have a sequence error” in the original head activator sequence, she wrote. The methods they had used at the time were “crazy, adventurous,” and in the end, she felt “we were close, but not correct.”

Her book came out in 2016, a self-published autobiography, titled (translated): Chica and Heinz Schaller, Life and Science. She is listed as the author, though she also credits a journalist with helping her interview and write.

I ordered a copy and spent a few days using Google Translate to convert it to English. I hoped it would tell me more about who Chica was, and I also wanted to see if she mentioned Müller. I found that the book supplied, with great candor, deep backstories for both her and Schaller. The book revealed that Chica’s mother had gotten pregnant out of wedlock and that she wanted to abort the child, but her father had threatened suicide if she did. She wrote that Schaller used to distill alcohol in the lab and distribute it to his colleague, and that Chica had once been in love with Klaus herself.

It also shockingly revealed that Klaus and AnnMarie married, and that Klaus later killed AnnMarie, their two children, and himself. It disclosed that Schaller had some sort of affair, that Chica had left him for a time, and that Chica and Schaller tried to have children, but could not. It confessed that Chica had fallen in love with other men during her marriage, and finally, that Chica and Schaller had once grown marijuana in their garden.

These details — save for the murder-suicide of AnnMarie and her family — are not all that shocking. A little home-distilled alcohol, a little marijuana, the ups and downs of a very long and seemingly successful marriage, a failure to have children: these are the things that make up many normal lives. But to someone like Müller, conservative as he appeared to be, these details might have appeared scandalous, as was her choice to publish them.

Her book also includes the history of her hydra work and her failed pursuit of a position in Heidelberg, though it does not mention the ugly university senate hearing. Müller is barely mentioned, except, notably, earlier in the narrative, when she is remembering her ascent in the developmental biology field. She writes: “Chica’s successes bring her not only invitations and an unfaithful husband, but also hostility. The latter escalates to accusations of fraud. They come from Werner Müller’s chair.”

That’s it, the only glimpse at what happened between the two of them in Heidelberg from her perspective.

Werner the Writer

Müller also turned toward writing as he aged. He published a book based on his life in 2021, roughly translated as Self-liberation from the Shackles of Church Religion, that provides insight into his background. Written under the nom de plume Frank Beiderbeck (the author biography notes that Frank Beiderbeck is actually “a professor emeritus at the University of Heidelberg” who has the real name “W.A.M.”), the book’s plot centers around Müller’s brother, who died young of leukemia.6

It is in his second book, published in January 2022, that Müller turned to the story that had been on his mind for decades. Entitled: The Price of Research, the book appears under the same pen name, Frank Beiderbeck, and contains what can be described as a crime story based on true events from a university institute in Heidelberg. The book’s biography likewise says the author was a professor of biological sciences at the University of Heidelberg and names his other books, including the “Self Liberation” book about Paul, directing readers to Müller’s Wikipedia page for more information.

What follows, if read as crime fiction, is poorly written. Character motivation is unclear, violence arrives out of nowhere, and the book has a confused chronology. But read as thinly veiled history — as it’s clearly meant to be — it’s fascinating.

Müller begins by writing that it should not be “too difficult for those interested to find out the real names of the protagonists of this story, especially since several known personalities, who were not entangled in the affair, are mentioned without pseudonyms.” Indeed, the name Alfred Gierer appears in the pages, as does Hans Meinhardt.

The book is narrated by a fictional journalist, telling the story of the university professor Michael Walter — an avatar for Müller. Amidst poisonings from lab-distilled alcohol and homegrown marijuana (echoes from Chica’s book), and copied laboratory protocols and the dead bodies that prop up the crime thriller plot, Walter is served with a letter “from the Ministry of State,” in which “a ministerial director announced that a disciplinary enquiry has been opened against him.” Walter is threatened with the loss of his position without benefits, and a fine of 40,000 euros, unless he declares in writing to “never again to remark publicly that Frau Dr Franziska Jansen had exhibited scientific misconduct and presumably committed fraud.”

Franziska Jansen, of course, is meant to be Chica.

The novel also tackles what transpired over the years for Gierer and Meinhardt, using their actual names, and also Jansen and various colleagues working on the activators and inhibitors of hydra generation. The book mounts a lengthy attack on the veracity of the head activator, using figures from Müller’s own work. There are chapters dedicated to nerve growth factors and the organizer discovery by Hans Spemann. There is a discussion of the Wnt pathway and a section where Michael Walter uses the head activator “synthetic product” bought from Bachem, and it “had absolutely no effect on his own animals.”

It also includes a description of Walter being asked to review a paper by Jansen; he criticizes the conclusion, and when the paper is resubmitted, the conclusion is not changed. The book includes scenes of an official hearing before a Senate, conducted in English, during which Walter struggles to communicate. Jansen (a “former translator”) has no problem.

The book is Müller’s version of the entire head activator story, protected behind a curtain of fiction. Near its end, Müller declares that “the truth had to be worked out in the laboratories of the world.”

Perhaps this has been done for Chica’s head activator. Steele told me he recently went to a hydra meeting in Germany. Not a single talk or poster at the gathering mentioned Chica’s peptide, he said. Head activation in hydra is still discussed in the community, but now in the context of the Wnt pathway. Science has shown that Chica’s head activator “is not encoded by a gene in a standard manner in hydra. That is clear, if it’s just not in the genome,” Steele said. So if Chica’s substance is somehow made in hydra, “it’s produced by some non-canonical method that I have a hard time conceiving of.”

However, this leaves open the question of what was really sequenced by Bodenmüller in the 1981 paper. It’s possible the substance came from bacteria that somehow contaminated Chica’s experiment. Perhaps that’s why the head activator was also found in mammals. But “it’s clearly not in anything that’s in GenBank, so it’s not in some common bacterium that contaminates lots of things,” Steele said.

Regardless, Steele knew Bodenmüller to be a careful protein biochemist who was “not just making this stuff up.” Steele said. The sample he used had proteinaceous material in it, and they got a sequence.

“That's the real puzzle to me,” Steele said. “How did they get that, or what it was that they sequenced, where it originated? And what organism makes it? It leaves you at the end with a feeling of … Is this something that’s ever going to make sense?”

At War and Peace

I once interviewed the great Eve Marder, a National Medal of Science winner and professor of Neuroscience at Brandeis University. She’s in her 70s now, but told me that when she was coming up in science in the late 1960s and ‘70s, she was often the only woman in a room full of men. She realized there were two ways women could handle this disparity. One was to be unfailingly polite, a lady at all times. The other, she said, was to constantly assert yourself and be combative. If you didn’t do that, you simply would not be heard.

It is difficult not to interpret Chica’s behavior accordingly. She came up in science when there weren’t many other women around. She’d been one of three girls in her high school class, among 30 boys. She’d followed Schaller around, the wife to his scientist, until she got a PhD herself. And she was the only woman in the Gierer lab.

That may have had something to do with Chica often being described as angry, dismissive of others, or unpleasant. She constantly had to kick down doors just to be in the room, and then had to raise her voice to be heard. Her biography includes passages aimed at the sexism she felt she’d endured, and she helped set up the Chica and Heinz Schaller Foundation in part to support young female scientists.

Steele met Chica in person just once or twice, but he confirmed this. “She was a woman fighting for space in the biological research sphere at a time when women in Germany were not taken very seriously in academics,” he told me. Yet as a young doctoral student in a lab full of more accomplished men, she’d performed a tedious, intensive experiment to isolate a substance that — in the moment — seemed to build a bridge between the worlds of developmental biology and modern molecular biology.

This is undoubtedly part of her story. The other part, however, remains her scientific legacy itself: her work on the head activator vexed many people in the field. I went looking for Cok Grimmelikhuijzen, the Dutchman who had been Chica’s postdoc. After failing to reach him, I finally emailed Frank Hauser, who had published papers with Cok. He told me Cok passed away in 2024, but Hauser remembered Cok calling the head activator an “unscientific fabrication.” Perhaps Cok had been “overly critical,” Hauser said, but those were his words.

Then there is Doug Fisher. He worked under Bode at UC-Irvine, and he did “everything one could imagine doing” to clone the head activator, he said, “and nothing worked.” The group at Irvine had a journal club that would discuss papers. Every so often, they’d read a paper that confused them, one where they didn’t understand the design, the controls, or the results, and then “everything would grind to a halt,” he told me. This happened enough times with papers from Chica’s group that Fisher began not to “believe anything that came from her lab” during that time.

That leaves Müller, her fiercest critic — should we believe him? Steele knew Müller, too, and once had dinner at his house. This was in 1993, when both were attending a hydra conference in Günzburg, Germany. Afterward, Steele and a couple of colleagues headed to Heidelberg. Müller drove them there and invited the group — along with Monical Hassel — over for dinner. Müller’s wife joined them, and the group had a “carefully orchestrated meal,” Steele said, of Zwiebelkuchen and Federweißer: onion cake and young wine from the fall harvest. The night was enjoyable, if “a little bit stilted.”

It’s possible that Müller simply disliked Chica and wanted to hurt her career. But it’s also possible that he was a quiet, somewhat stiff person who had replaced religious dogma with research. And because of this, perhaps he felt he had to stand up for the purity of science.7

Berking told me that Müller “was hurt by [Chica],” and “tried to digest” their horrid interaction for years. “Eventually, he wrote this book for himself,” Berking said. “It was for him to write down his side of the history.”

Berking told me Müller didn’t show him the book until sometime after he had self-published it. “That was strange for me, that he gave it to me not immediately,” Berking said. “I was involved, too, in this problem.”

It’s that image, more than any other, that sums up the great drama of the head activator for me. More than 30 years after the head activator made its scientific splash, decades after Müller had been called in front of the university senate, and more than fifteen years post-retirement from Heidelberg, he was still thinking about it. Müller, writing up his story even after Chica’s death and not all that far from his own, in September 2022. Müller, handing this thinly veiled fiction over to Berking as if to say:

“Remember what happened back then, with the hydra? I want you to read this.”

Correction: A prior version of this article stated that Stefan Berking was a student in Chica Schaller’s laboratory. We have corrected this error.

Brady Huggett is the features editor at The Transmitter, and a contributing editor at Asimov Press. He is also the writer and producer of the limited series podcast, Hope Lies in Dreams.

Thank you to Andrea Weaver for translating The Price of Research book, and Nicholas Huggett for help with additional German-to-English translations. The header image was made by Ella Watkins-Dulaney.

Cite: Huggett, B. “Mystery of the Head Activator.” Asimov Press (2026). DOI: 10.62211/28kw-72nq

Further Reading:

• Chica und Heinz Schaller — Leben und Wissenschaft. By Chica Schaller. Copyright 2016, Chica Schaller.

• Hydra and the birth of Experimental Biology — 1744. Abraham Trembley’s memoirs concerning the natural history of a type of freshwater polyp with arms shaped like horns. Sylvia G. Lenhoff and Howard M. Lenhoff. Copyright 1986 by the Boxwood Press.

• Selbst-Befreiung aus den Fessein der kirchlichen Religion. Erzählung. Frank Beiderbeck. Copyright NOEL-Verlag.

By Andrew Hunt

When the researchers at Google DeepMind unveiled AlphaFold3 in Nature in May 2024, they did something controversial. Instead of releasing the code to enable other researchers to verify and build upon their protein structure prediction model, they restricted access via a web server.

The computational biology community erupted. More than 1,000 researchers signed an open letter condemning the decision as a failure to follow scientific norms. Roland Dunbrack, a computational structural biologist who reviewed the paper, called the decision “an incredible disservice to science.” The backlash worked, and DeepMind released the code in November 2024.

When it comes to wet lab research, however, we’ve been withholding our “code” for centuries with no outcry. Unlike computer code, which captures a model’s process in machine-readable format, biological protocols operate through layers of human interpretation and tacit knowledge. Seemingly trivial details, such as the brand of plastic tubes used, are often lost in translation from bench to page and can hinder attempts to reproduce the results.

In theory, we already have a solution to this problem. Critical experimental details should be provided in the Methods section of scientific papers (part of the standard IMRaD structure: Introduction, Methods, Results, and Discussion), where researchers outline procedures in sufficient detail for others to evaluate, replicate, and build upon their work. And yet, the canonical Methods section is flawed. In 2021, the Center for Open Science found that none of the 193 cancer experiments they examined were “described in sufficient detail to design a replication without seeking clarifications from the original authors.”

Such findings illustrate science’s systematic failure to value and communicate the “how” of research. The scientific community celebrates discoveries but often treats the experiments that generate them as mere housekeeping, relegating their methods to supplementary materials or omitting them entirely.

Insufficient methods limit cumulative scientific capabilities. When researchers spend months trying to reproduce something that should take days, or when improved techniques are shared only among well-connected labs, time is wasted rebuilding foundations rather than advancing the scientific frontier.

This isn’t a modern problem, either. Scientists have struggled to transfer capability for centuries, as it is usually more difficult than transferring concepts. It requires capturing “tacit” knowledge and equipping new human hands to execute it. Furthermore, our primary scientific communication tool, the journal article, has increasingly been optimized to stake claims and present results, rather than to help researchers build on one another’s work.

As the scientific community wrestles with how to reform scientific publication, tracing the evolution of the Methods section can help us understand why it so often fails and how we might improve it.

Ancient Methods

Millennia before scientific journals existed, a Babylonian cook pressed cuneiform into clay, preserving one of the world’s oldest known recipes: “Stew of lamb. Meat is used. You prepare water. You add fat. You add fine-grained salt, dried barley cakes, onion, Persian shallot, and milk.”

This clay tablet, dated to 1730 BCE, was terse and practical. The instructions written on its surface, however, mark the conceptual birth of the Methods section. With the invention and spread of writing, farmers, cooks, artisans, perfumers, architects, and engineers began to record the methods and knowledge of their trades.

For most of antiquity, written instructions focused on practical skills, such as farming and cooking, rather than science. “The separation of craft know-how from more theoretical knowledge was characteristic” of the ancient world, observes historian Pamela O. Long in her book, Openness, Secrecy, Authorship. This division was reinforced by philosophical hierarchies, such as Aristotle’s Intellectual Virtues, where theoretical wisdom outranked practical excellence.

The divide also had deep social roots. “Ancient crafts, carried out for the most part by slaves and manumitted slaves, suffered from a profoundly low status,” Long writes. Two parallel traditions of knowledge emerged, which rarely intersected, one by and for practitioners focused on specific tasks and the other by philosophers pursuing a deeper theoretical understanding.

Work by the Roman architect Vitruvius (c. 80 BCE to c. 15 BCE) served as an early bridge between craft and philosophy. A military engineer turned architectural theorist, Vitruvius wrote De Architectura to document Roman building practices spanning both architectural design and engineering. Vitruvius insisted that architecture requires both “ratiocinatio” (reason) and “fabrica” (fabrication), and he warned against those who pursue only manual skill without theoretical understanding, who “do not reach a position of authority corresponding to their labor.” Vitruvius equally railed against those who rely only on theory without practice, who “seem to follow a shadow rather than substance.”

This fusion of practical skill and scholarly inquiry gradually reshaped the pursuit of knowledge itself. Vitruvius’s integration of “how” and “why” eventually matured into the scientific method.

Another example of such a thinker is Ibn al-Haytham (965-1040), a mathematician and astronomer who pioneered experimental methodology during the Islamic Golden Age. When al-Haytham rashly claimed to be able to control the Nile’s flooding, the Fatimid Caliph al-Hakim invited him to Cairo to demonstrate. After surveying the river, al-Haytham realized the task was impossible and allegedly feigned madness, accepting house arrest to avoid the ruler’s wrath. Whether apocryphal or not, his decade of confinement in Cairo (1011-1021) proved productive.

During his house arrest, al-Haytham did a series of experiments that culminated in his Book of Optics. Using a pinhole camera, he studied both eclipses and human vision, discovering the geometric principles governing optics. He documented not only his insights but also his doubts, failures, and, crucially, his process:

The experimenter should bore two holes in the wooden block. One of these should be from the outermost of the two near circles to the outermost and opposite circle of the two circles on the other surface. Let the hole be circular and cylindrical, and let its circumference coincide with that of the two facing circles. This hole, then, will be at right angles to the two parallel surfaces.

Al-Haytham’s careful description of his methods enabled others to replicate and build upon his work centuries before European scientists adopted similar practices.

During the Middle Ages, the economics of craft work shifted, laying the groundwork for the modern concept of intellectual property. In her book, Long notes that medieval cities established craft guilds to regulate trades, fostering a proprietary attitude toward technical innovation. Venice’s glassmaker guild, for example, became Europe’s premier luxury glass manufacturer during the early Middle Ages.1 Their sophisticated processes made Venetian glass so valuable that, by 1474, Venice enacted Europe’s first statutory patent system, thereby establishing a legal framework in which guild secrets and state-granted monopolies reinforced one another. (Venetian glass was so profitable, in fact, that the government threatened glassmakers with death if they shared trade secrets or left the island.)

This tension between protecting and sharing craft knowledge pervaded early scientific practice. Galileo (1564-1642) illustrated this well when, in 1610, he published Sidereus Nuncius, announcing his telescopic discovery of lunar craters to secure priority and patronage while deliberately withholding his telescope-making techniques to maintain a competitive advantage.2 It was only until decades later, when his reputation was assured, that he felt comfortable publishing his methods in craftsman-like detail in his final book: Two New Sciences.3

Robert Boyle (1627-1691) took the opposite approach from Galileo’s, making transparency itself a part of his method. With his assistant Robert Hooke, he built an improved air pump based on Otto von Guericke’s design, creating a vacuum chamber that could be opened and resealed for repeated experiments. Inside it, they witnessed striking phenomena: sound was muffled, flames were quenched, and water boiled at a lower temperature. These observations led to his discovery of the pressure-volume law that bears his name.

When philosopher Thomas Hobbes dismissed these experiments as trickery, insisting reason alone revealed truth, Boyle responded with public experiments and exhaustive documentation. His New Experiments Physico-Mechanical was self-admittedly “unnecessarily prolix,” documenting every detail needed for replication.4 Boyle proposed a new model in which experimental knowledge was validated through collective observation rather than individual authority.

Such variability in openness reflected a fundamental trade-off. Early scientists recognized that knowledge sharing enabled collective progress. Yet, their economic survival was grounded in patronage, and patrons (and the scientists themselves) sought priority claims for discoveries. While full disclosure helped science advance, it also risked letting competitors replicate and surpass one’s own work.

Science Formalizes

Books, the primary medium for scientific communication at the time, fundamentally shaped how experimental practices were transmitted. Scientists could include extensive detail, but this required composing full-length treatises. Publishing and distribution were slow; years could pass between observation, publication, and verification attempts.

Boyle’s battles with skeptics highlighted the need for rapid and reliable sharing and verification of experimental work. This vision materialized in 1660 when Boyle and his colleagues founded the Royal Society, a public forum for discussing and witnessing experimental results. With their motto “nullius in verba,” meaning “take nobody’s word for it,” they planted the seeds for what would eventually grow into the modern scientific journal.

In 1665, Henry Oldenburg, secretary of the Royal Society, launched Philosophical Transactions, a journal dedicated to chronicling and disseminating research.5 Early publications read like open letters, ranging from half-page notes to forty-page treatises: Antonie van Leeuwenhoek’s report on “little animalcules,” Caroline Herschel’s comet discovery (originally addressed to friends, mixing personal observations with methodological descriptions), and even Benjamin Franklin’s kite-and-lightning experiment, which was published in the form of a letter to the botanist Peter Collinson. In the letter, Franklin promised electricity would “stream out plentifully from the Key on the Approach of your Knuckle,” blending a dramatic demonstration with practical instruction.

Transactions, however, still displayed the tension between openness and secrecy. Despite “nullius in verba,” early journals had no requirement regarding the information authors were expected to include. Leeuwenhoek famously kept his lens-making techniques to himself, declining to share “other glasses and other methods (which I reserve to myself alone).” When faced with skepticism from the Royal Society about creatures so small that “millions of millions might be contained in one drop of water,” he assembled eight witnesses to peer through his microscopes and sign affidavits rather than reveal his blueprints.

Leeuwenhoek’s approach typified early scientific communication: scientists often emphasized their findings rather than the means by which they arrived at them, and they did so in idiosyncratic ways. However, over the course of the nineteenth century, this style of documentation gradually gave way to structured scientific reports as science evolved from a pursuit of the wealthy into a professional discipline. The term “scientist” itself was only coined in 1833, as universities began establishing dedicated science programs6 and consistent measurement standards emerged to enable researchers to compare results more easily.7

Tracking this stylistic evolution, Dwight Atkinson analyzed Philosophical Transactions in his book Scientific Discourse in Sociohistorical Context, finding that “methods descriptions underwent dramatic growth in the 19th century, and an overall theory → experiment → discussion organization was evidenced commonly for the first time.”

Meanwhile, the scientific community expanded from intimate circles of correspondents to a broader network of practitioners. Atkinson notes that detailed Methods sections became crucial for establishing credibility as researchers could no longer personally vouch for unfamiliar colleagues in distant places. This social expansion coincided with technological advances in printing and distribution, as evidenced by the dramatic growth of scientific journals: from approximately 100 in 1800 to over 10,000 by 1900. Together, these pressures of scale and speed pushed scientific writing toward increased efficiency.

Nineteenth-century scientists adapted to this growth by introducing fast, short-form outlets alongside traditional narrative journals, epitomized by the Comptes Rendus of the French Academy of Sciences, established in 1835, with strict page limits to enable rapid weekly publication.

The French microbiologist Louis Pasteur embraced this emerging style of publication. A fierce combatant in scientific debates, Pasteur regularly sparred with rivals Auguste Trécul and Edmond Frémy in heated exchanges at the French Academy of Sciences. He had a gift for dramatic demonstration, famously proving the efficacy of his anthrax vaccine through live challenge trials before crowds of farmers and journalists.

Pasteur’s approach stemmed from the conviction that empirical evidence must prevail over theoretical speculation. His vow, “to demolish M. Frémy’s theory [of spontaneous generation] by a decisive experiment on the juice of grapes,” captured this commitment. Pasteur published rapid-fire notes in the Comptes Rendus to publicize and defend his fermentation findings, several of which included concise experimental recipes. His work culminated in his 1876 book Études sur la bière (Studies on Beer), where he provided an exhaustive description of his methods in order to confidently proclaim that “the hypothesis of MM. Trécul and Frémy … is annihilated.”

Pasteur’s organization anticipated the IMRaD sections we have today. And he was not alone in his use of such a format. Earlier researchers like Faraday and Joule also often used the “theory → experiment → discussion” format, providing detailed method descriptions in their Philosophical Transactions publications.

As this approach gained popularity, the growing number of scientists and the increasing complexity of their work led to dedicated venues for sharing methodological knowledge. Several method-centric periodicals were established, including the Journal of Applied Microscopy, founded in 1898, which provided recipe-style descriptions of research. Its first edition, for example, contains W. W. Alleger’s improved method for preparing agar: “Pour a liter of water over a pound of finely minced lean beef … Rub up ten grams of powdered agar in a little cold water … stir this into the filtered meat-infusion and place it on the fire.”

By the late nineteenth century, methods had started to shift from trade secrets to a primary currency of scientific credibility. Methods, in other words, became a type of knowledge worthy of preservation and dissemination, independent of theory or results.

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The Modern Journal

This emphasis on methods, however, did not persist into the 20th century. Both the Philosophical Transactions of the Royal Society and spectroscopic articles in Physical Review began devoting less text to methodological details. Where 19th-century scientists had used detailed procedural descriptions as a central persuasive strategy, 20th-century authors increasingly prioritized theoretical frameworks and the interpretation of results.

This transformation resulted from converging forces. Mounting financial pressures drove journals toward shorter, “Proceedings-style” publications, such as the Comptes Rendus, requiring authors to economize on methodological details. These pressures were acute as journals, whether commercial or privately sponsored, were typically not profitable before the 20th century.8

Meanwhile, experimental science had matured to the point where researchers could cite methods compendia or prior literature rather than reproduce multi-page procedures, assuming readers were competent practitioners well-versed in their respective specialties. This change illustrated an implicit reliance on shared professional context. Methods moved to the background.

This push for efficiency sparked fierce debates across disciplines. Many journal editors in the 1920s were swamped with lengthy and poorly written submissions. In 1928, the National Research Council convened conferences to explore the standardization of article formats, sparking debate about the balance between efficiency and creativity. Harry Hollingworth, chairman of the New York City committee, delivered a passionate minority report condemning standardization: “If we insist upon cramping [the scientist’s] style and insisting upon arbitrary form, censorship, and the like, we may make uniform pages, but we kill the life of science.”

Despite such critiques, practical needs prevailed. As publisher Edward Passano stated, “The main purpose of this conference is to effect economy in publication.” Psychologists were likely the first to adopt a standardized journal article format. In 1928, the American Psychological Association released a “publication manual” recommending a “natural order” for submissions: (1) statement of conditions (subjects, observers, apparatus, set-up), (2) course of experiments, (3) statement of results, and (4) discussion of results and conclusions, codifying the modern IMRaD structure. The Methods section framework is remarkably close to its current form, stating it should be “technical, concise and not repetitive” while providing “sufficient detail to enable [the reader] to reconstruct and to criticize the experimentation and to compare it with other procedures and results.”

The push toward standardization spread across disciplines throughout the 20th century. World War II and the 1957 launch of Sputnik prompted the U.S. government to significantly increase its research and development (R&D) budgets, resulting in a more than 70-fold increase over pre-war spending. This triggered rapid growth in both the number of scientists and the volume of scientific publications. In 1945, Vannevar Bush, the first U.S. presidential science advisor, captured the feeling of the moment: “There is a growing mountain of research … The investigator is staggered by the findings and conclusions of thousands of other workers.” Just as psychology struggled with publication overload in the 1920s, the entire scientific enterprise now faced a similar crisis.

To manage this flood of publications, journals enforced structural requirements. Medical journals led this trend, with section headings first appearing around 1940 and becoming ubiquitous by the 1980s. The IMRaD structure was formalized by the American National Standards Institute through two key standards in the 1970s.9 As authors Day and Gastel explain in How to Write and Publish a Scientific Paper, the new format guides authors to communicate “what they did, why it was done, how it was done (so others can try to repeat it), and what was learned from it.”

Yet even as IMRaD became standard, the Methods section struggled to fulfill its promise. From 1960 to 1970, the annual number of U.S. PhDs awarded grew at over 13 times the rate of population growth, straining the person-to-person apprenticeship system for training new scientists. Furthermore, page limits and increasing methodological complexity meant that modern techniques were often not effectively communicated in typical journal Methods sections.

This gap between what researchers needed and what journals provided sparked the founding of new venues dedicated specifically to methods: Methods in Enzymology (1955), Methods in Molecular Biology (1983), and eventually Nature Protocols (2006). Following in the footsteps of the Journal of Applied Microscopy and others, these publications aimed to accelerate the dissemination of methodological knowledge between researchers.

While they improved the spread of methods, they couldn’t ensure completeness. Even when mainstream journals began requiring Methods sections in the 1980s, researchers still often failed to include key details. The consequences proved particularly severe in medicine, where incomplete reporting could affect patient care. In response, a coalition of medical experts developed the CONSORT Statement in 1996, a checklist and flow diagram for tracking participants through clinical trials.10 Doug Altman, one of CONSORT’s architects, captured its philosophy: “Readers should not have to infer what was probably done; they should be told explicitly.”

The checklist approach proved effective. A review of over 16,000 randomized controlled trials found that endorsement of the CONSORT guidelines improved 25 of 27 measured reporting outcomes.11 Other disciplines sought similar standardization of their Methods sections, eventually leading to initiatives such as the Materials Design Analysis and Reproducibility Checklist and the STAR Methods (which are still widely followed by major journals today).

Digital Evolution

In the 1990s, as the internet became more widely adopted, the marginal cost of publishing effectively dropped to zero. Journal editors began taking their publications online and introducing supplementary materials, while maintaining concise and results-driven main articles.12

Unfortunately, this migration of Methods sections to supplements proved problematic. While authors could share richer method details, these spaces were lightly reviewed and ill-structured, with untraceable citations and unstable links.13 Sometimes supplements disappeared entirely after publication, prompting efforts to establish better standards for preserving them.14 In response, some journals (such as Nature) reversed course by reintegrating full Methods sections directly into their online articles rather than relegating them to easily lost supplementary files.

While digital publishing expanded the space for detailed methods, a more significant challenge for thorough methods remained: tacit knowledge. Written instructions still failed to fully capture the embodied or unconscious expertise essential to success. In 2003, Princeton PhD student Moshe Pritsker spent more than a month attempting to grow mouse embryonic stem cells using published protocols. Frustrated, he flew to Edinburgh to learn the technique from the original team, discovering that the trick was simply “handling” cells properly, something easily demonstrated but difficult to describe in text.

This experience inspired Pritsker to launch the Journal of Visualized Experiments (JoVE) in late 2006. JoVE’s first issue featured 17 peer-reviewed videos showing science techniques. Today, JoVE’s library has over 25,000 videos. Despite demonstrating that video can clearly communicate scientific techniques, barriers such as cost, production time, and institutional inertia have prevented it from becoming the de facto standard for sharing research methods.

Around the same time that JoVE appeared, MIT graduate students in the Endy and Knight labs made their own discovery about sharing scientific knowledge. These engineers-turned-biologists found that essential laboratory techniques, especially in synthetic biology, weren’t being documented in protocol manuals but instead were “passed around as lore.” In 2005, they launched “Endipedia,” an internal wiki for sharing research methods that later evolved into OpenWetWare, the first public wiki dedicated to scientific protocols.

OpenWetWare shared many features with Wikipedia, including version histories, real-time editing, and distributed collaboration. The platform quickly gained users beyond MIT, becoming a living, crowdsourced repository of scientific methods.15 Despite its practical value, however, the project faced a challenge confronting many new resources: It existed outside academia’s prestige system. Contributions couldn’t be easily cited, and entries lacked persistent identifiers, making it difficult to track or reward ideas over time.

Even with NSF funding, OpenWetWare was unable to sustain itself. The money ran out on April 15, 2025, forcing the servers offline for six months. As of this writing, the site has come back online, though its long-term future remains uncertain.16

Still, OpenWetWare demonstrated that researchers will openly share bench protocols online, and nearly a decade later, protocols.io picked up the baton. In a familiar pattern, MIT postdoc Lenny Teytelman spent a year and a half correcting an error in a published microscopy protocol after discovering that a reagent volume needed to be quintupled and incubation time quadrupled, for which he received no academic credit.

In 2014, Teytleman, along with his cofounders, launched a Kickstarter campaign for protocols.io to address this deficit. Their mission was to build “a free, central, up-to-date, crowdsourced protocol repository for the life sciences.” Inspired by GitHub, the vision was to prevent wasted time and improve reproducibility by allowing researchers to publish and receive credit for refinements that are typically lost in notebooks or buried in supplements.

Protocols.io has grown into a significant repository of research methods, hosting approximately 15,000 publicly available protocols and earning endorsements from numerous journals. However, maintaining this resource has proved financially challenging. The platform experimented with a “freemium” model, in which the free tier assumes researchers are ready to publish openly. Those who prefer to refine privately first encounter strict limits and are prompted to upgrade to paid plans.17

By 2023, after nine years of struggling to balance openness with sustainability, the platform was sold to Springer Nature. The acquisition brought financial stability but came at a cost: subscription prices surged 700 percent for 2025 under the new ownership, undermining the platform’s founding commitment to the accessible sharing of methods.

Despite more than a decade of effort, published protocols remain second-class research outputs. They are still optional in most fields, with weak incentives and minimal academic credit for method development. While such digital platforms haven’t solved the second-class status of methods, they have transformed the way many researchers share procedures, making methods more accessible, searchable, and citable, while fostering new expectations for openness. Importantly, they’ve also shown that researchers can devise ways to improve the delivery and reception of the Methods section.

A Better Marketplace For Methodology

Doug Altman, of CONSORT checklist fame, captures the predicament with modern methods well: “Everyone is so busy doing research they don’t have time to stop and think about the way they’re doing it.” Pausing to improve how we work might seem like a distraction from science, but in fact, it is central to its progress. Discovery is inseparable from the tools and techniques that enable it. Yet, we routinely undervalue both the creation and diffusion of such methods.

At this point, one might expect me to recommend keeping better lab notebooks or writing better methods sections. But this is not the answer in and of itself. Research is inherently exploratory and context-dependent. We don’t know in advance which details matter, and we often can’t take the time to document everything. Nor should we, as we want progress, not paperwork.

Still, doing our own research and helping others do theirs is often framed as a trade-off. In the short term, it is; resources are finite, and time spent on one subtracts from the other. But science itself is a long-term endeavor. Instead of accepting the trade-off, we can invest in infrastructure that expands what’s possible for both: systems that enable method transfer and incentives that reward the sharing of methods.

Software offers one example. Code that others could inherit and extend didn’t come from asking developers to document more. Rather, it originated from tools such as Git and GitHub, which made record-keeping a byproduct of work. Git is akin to plumbing; it tracks every change to code, lets developers revert to earlier versions, and merges contributions from different people. GitHub is the social platform on top, where developers share code, discover each other’s work, and build reputations. Together, they make collaboration more frictionless, and because contributions were trackable, they became valuable.

Protocols.io aimed to be the GitHub of biology, but GitHub could only exist because Git came first. Biology as yet has no equivalent foundation. Git works because code is digital; the instructions themselves are what get executed. Hardware varies, but it’s standardized enough that the same script runs the same way on any compatible machine. But wet lab biology is different. A protocol describes a process, but it isn’t the process itself. Between the instructions and the result stand human hands, variable equipment, and the unpredictability of biology. We have no infrastructure for capturing physical work, and little that makes method transfer meaningfully easier.

Fortunately, the research community is already experimenting with solutions on multiple fronts.

New technologies are finally equipping us to capture tacit knowledge in the laboratory. Cultivarium’s PRISM system, for example, uses smart lab glasses that record a researcher’s process in real time, capturing visual cues, timing, and movements that written protocols often omit.

Other groups are adding context and explanation to scientific results and methods. Arcadia Science, for instance, publishes “pubs” hosted on protocols.io that integrate step-by-step instructions, as well as the rationale behind decisions, hurdles encountered along the way, and experiments that didn’t work. For computational work, they convert Jupyter notebooks directly into publications, making the analysis itself executable.

Automation could do the same for the wet lab, translating a researcher’s craft knowledge into explicit instructions that others can execute. However, most lab automation efforts have been designed to scale volume (e.g., by running thousands of identical samples) rather than to scale variety in experiments. Cloud labs promise to make wet-lab work as accessible as running code, with new techniques available at the click of a button. So far, however, they fall short. Research demands constant iteration, but current cloud labs make such tinkering tedious (although these may be early growing pains). The next generation of automated labs will need to provide structure while enabling responsiveness.

Other efforts to produce better infrastructure are emerging from new institutional models. As traditional grants primarily reward new findings rather than shared know-how, they rarely make tool- and protocol-sharing a genuine, enforceable requirement. Focused Research Organizations (FROs) such as Cultivarium, Align, and E11 Bio operate under a different model. They exist outside the standard academic marketplace and are explicitly funded to develop tools, techniques, and datasets that enable the community. While nascent and experimental, FROs represent one way to address the infrastructure gap. If we want shared methods, we need funding streams that make genuine methodological openness a condition of support.

But better infrastructure is only part of the answer. We also need to reshape scientific incentives around generativity rather than novelty. By generativity, I mean how much a contribution unlocks the work of others. Consider the microscope. Its value lay in the capability it gave others to see what couldn’t be seen before, paving the way for Leeuwenhoek’s “little animalcules,” Pasteur’s germ theory, and modern cell biology. That’s what we should be measuring and rewarding.

Rewarding generativity requires seeing it first. Citations get us partway there, but they’re a crude proxy for capability transfer. A citation tells you that someone referenced your method, but not whether they successfully executed it. It can’t distinguish between a protocol that worked immediately and one that took six months of troubleshooting. Worse, citations mostly point to frozen artifacts, a paper fixed at the moment of publication. But methods should be living things, refined and improved through use. A citation alone can’t capture that evolution. The information flows out, but nothing flows back, leaving the community blind to what is actually working.

Sharing methods as executable artifacts could help repair this broken feedback loop. When adoption becomes visible and modifications trackable, improvements can flow back to the source, thus letting us measure and reward the process of science rather than just its outcomes. If we can see how a method evolved through use, who made it transferable, and how much a contribution enabled others’ work, then we can finally give credit not only to those who publish first, but also to those whose methods actually worked for others. Sharing stops feeling like giving away a competitive edge and starts feeling, instead, like investing in a commons that you yourself depend on.

Building infrastructure that makes this possible might sound expensive, but consider the hidden costs of our current system. The U.S. alone invests an estimated $28 billion annually in irreproducible biomedical research. Methods are only a piece of the irreproducibility puzzle, but they’re a contributing factor. Even modest improvements could justify the investment in infrastructure. Meanwhile, academic publishers earn billions, with some of the highest profit margins in any industry. There is money available; we just need to funnel it towards infrastructure that actually benefits researchers.

This vision isn’t new, but our capacity to realize it is. Three centuries ago, Robert Boyle advocated making experimental details public, believing that shared capability would benefit discovery. We now possess technologies he couldn’t have imagined when writing his “unnecessarily prolix” methods: video, the internet, automation, version control, and machine learning. Yet, we’ve barely begun to harness them for method sharing.

As we build a better future, we can take comfort in Boyle’s encouragement to his fellow experimenters: “though some of your experiments should not always prove constant, you have divers[e] partners in that infelicity, who have not been discouraged by it.”

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Andrew Hunt is a methods and measurement nerd and a postdoctoral fellow in the Baker Lab at the University of Washington, where he designs new proteins from scratch.

Cite: Hunt, A. “Inventing the Methods Section.” Asimov Press (2025). DOI: 10.62211/92kw-71iw

Thanks to Niko McCarty and Xander Balwit, who helped me transform this idea into a publishable essay. I’m also grateful to Harley Pyles, Henry Lee, Don Hilvert, Amir Motmaen, and Grant Landwehr for providing feedback on drafts. And thank you, finally, to Jon Bogart, Anna Marie Wagner, and Renee Wegrzyn for conversations that influenced the ideas here. Header image by Ella Watkins-Dulaney.

This is the first article of Issue 09. Read our Editor’s Note to preview upcoming articles, which will be published every Monday.

By Robert Reason

Science seeks truths that outlive those who discover them. English poet William Wordsworth’s observation that “to the solid ground of nature trusts the Mind that builds for aye [forever]” — a line that appeared beneath the masthead of the scientific journal Nature for 75 years — captures this romantic ambition: the dream that building on nature’s foundations yields truths durable enough to transcend their discoverers.

And yet, for many of us, when we think about scientific prestige, we cannot help but focus on the individual. Often, we imagine institutions such as Oxford or Harvard as metonyms for the “brilliant mind,” or perhaps envision a Nobel Laureate or Fields Medal winner. One component of this prestige is selectivity — from many, few are chosen. The same is true for scientific journals. While both journals and individuals project their prestige through reputation, journals have found ways to signal prestige through metrics such as impact factor, acceptance rate, and journal rankings; each suggesting the difficulty of publication and the likelihood that an individual’s work will receive institutional acclaim as a result.

At the dawn of the 19th century, approximately 100 scientific periodicals existed worldwide, and by its close, this number had risen to an estimated 10,000. Such growth marked a new era of independent scientific periodicals, distinct from traditional society publications. In such a competitive landscape, most of these publications clung to a tenuous existence, with prominent titles like The Reader (founded 1863) and Scientific Opinion (1864) struggling financially before ultimately folding. Even established and reputable periodicals, such as Philosophical Transactions of the Royal Society, which had enjoyed royal patronage since it was formally taken over by the Royal Society in 1752, rarely made money and struggled to publish without assistance.

When Norman Lockyer and Alexander Macmillan launched Nature on November 4th, 1869, they did so amidst a graveyard of failed scientific periodicals. That Nature survived while so many publications collapsed reflects not only scientific merit, but patronage, elite networks, speed of publication, and a talent for capturing an international audience.

From these advantages emerged not only a successful journal but also a system of prestige that continues to shape modern science. Prestige in this system is not simply a reflection of pure scientific merit, as one would hope, but a fiction that attempts to command attention in an era where the quantity of research far exceeds an individual’s capacity to assess it.

Today, this system faces serious scrutiny, with many questioning whether selective journals serve science beyond merely rationing merit. Understanding how Nature’s prestige was constructed, however, can help clarify which elements are deserved and which are entrenched.

Founding Nature

Many of the features that would come to define Nature emerged in its earliest years. Survival was not inevitable, ultimately resting upon three contingent advantages: patronage that insulated it from commercial failure, elite networks that conferred early credibility, and a publication speed responsive to the increasingly competitive scientific environment.

Initially, what distinguished Nature from its failed contemporaries was the patronage of Alexander Macmillan, who, alongside his brother, had built Macmillan & Co. into one of Britain’s most successful publishers. Flush from a remarkably profitable decade built on fiction, theological texts, and educational works, Macmillan was eager to expand his empire and could afford to absorb the financial losses that would have buried other periodicals (which he did, for the thirty years before Nature began turning a profit).

Macmillan already knew Lockyer. Indeed, Lockyer’s Elementary Lessons in Astronomy (1868) had sold well for Macmillan, who then employed him as his most important “consulting physician in regard to scientific books and schemes.” Lockyer was at the zenith of his early career, co-discovering helium with Pierre Jules Janssen in 18681 and elected as a Fellow of the Royal Society in 1869.

Had Lockyer’s reputation not been what it was, Nature would have perished. Patronage secured survival, but credibility required connection. Lockyer’s prior editorship of The Reader had linked him to influential scientific circles, most notably the English biologist Thomas Huxley and the X-Club. This informal dining society of nine prominent scientists, formed in 1864 and meeting monthly, exercised considerable influence over British scientific institutions and publications, promoting scientific naturalism and working to establish science as a professional, secular discipline independent of ecclesiastical authority.

Huxley, alarmed by scientific errors in popular books and frustrated by theological overtones he believed many journalists (particularly women) wove into their writing, concluded that only researchers themselves could properly educate the public. Through his enthusiastic support, Nature found an early contributor with an interest in scientific journalism unusual for a man of his scientific stature. Huxley, for his part, relished the attention, musing that when it came to journalism, he was “as spoiled as a maiden with many wooers.” Huxley also encouraged other prominent figures to contribute, even though they generally preferred to publish lengthy scientific essays in more established monthly periodicals.

While attracting prominent contributors was beneficial, the early editorial approach of Nature was unconventional. Lockyer envisioned the journal serving two audiences: educated laypeople seeking accessible science and professional researchers eager to learn about the latest advances.

Avoiding the abstract, passive voice of specialist journals, many popular articles in Nature were written in an accessible first-person, journalistic style. Observations from readers of a decidedly less technical nature were featured, including a report of a pigeon’s cunning method of procuring food by repeatedly startling a horse to shake grain from its nose-bag and an account of a goose raised by a Golden Eagle and taught “to eat flesh.”

Gradually, such whimsical observations yielded space to more technical book reviews and papers. Lockyer, who had hoped for favor from both the intellectually sophisticated layman and the scientific community, found that he mostly attracted the latter. Nature became a publication with short publication cycles and brief articles, with little elaboration or color.

Many scientists viewed these changes positively, regarding Nature as an efficient means to highlight a scientific idea. Capturing this sentiment, William Crookes, who would later become President of the Royal Society and one of the discoverers of Thallium, requested in an 1895 letter to Lockyer that his paper on helium’s spectrum appear in Nature even though it would already be published in his own Chemical News: “my circulation is not to the same class of researchers as that of ‘Nature,’ and having taken a great deal of trouble about it I want the results to get to the right people.”

Nature had cultivated this readership of active researchers through publication speed: its weekly schedule made it essential reading for scientists tracking developments in increasingly competitive fields. As to why such speed was possible, one likely factor was economic. Macmillan absorbed the financial losses that more frequent publication required, losses that would have crippled competitors, while society journals generally operated on quarterly schedules tied to meeting proceedings, creating inherent publication delays.

The strategic utility of this model became evident in how researchers employed the journal. One example was George Romanes, a seminal figure of comparative psychology and popularizer of “neo-Darwinism,” who presented his theory of “physiological selection” to the Linnean Society in May 1886 before publishing detailed abstracts across three consecutive August issues of Nature to establish priority.

The success of Nature’s approach was recognized internationally, with the first editor of Science declaring his desire that it may “in the United States, take the position which Nature so ably occupies in England, in presenting immediate information of scientific events.”

Speed of publication would have meant little, of course, without credibility. Although Nature initially drew legitimacy from its X-Club connections, this proved fragile. Lockyer’s commitment to editorial independence conflicted with the Club’s expectation that the journal would reliably advance its interests. Disputes followed, beginning in 1872 with the Hooker-Owen controversy, where Nature published Joseph Hooker’s defense against Richard Owen’s accusations of mismanaging Kew Gardens, and then gave Owen space to respond with his rebuttal. Hooker, a prominent X-Club member, regarded the platforming of his opponent as an act of disloyalty, while Lockyer argued that the journal could not be “the mere mouthpiece of a clique.”

Thoroughly annoyed with Lockyer and losing much of their initial enthusiasm, the X-Club’s contributions to Nature began to decline, further isolating the publication’s lay readership by depriving them of the popular articles the Club had regularly provided. Yet this development did not significantly undermine Nature’s credibility within the scientific community. The X-Club still faced opposition from many important scientists who continued to contribute to the journal, while the Club’s own influence was waning due to internal conflicts and its aging membership, leading to its disbanding in 1892.

More significantly, a new generation of scientists was beginning to assume leadership of the British scientific community, and this cohort would include some of Nature’s most important and prolific contributors of the late nineteenth century, such as eminent zoologist Ray Lankester, physicist Oliver Lodge (a giant in radio communication), and George Romanes, a protégé of Darwin.

Unlike their predecessors, whose preferred medium for scientific debate tended to be long-form periodicals, this new generation generally preferred Nature, often redirecting debate to its pages. Debates were structured, combative exchanges, featuring formal turn-taking and explicit rebuttals.

One noteworthy debate centered on Weismann’s theory of panmixia, which proposed that when an organ no longer conferred an evolutionary advantage, that organ would no longer be the subject of natural selection, leading it to diminish in size or vanish entirely. George Romanes endorsed this view in Nature, prompting Lankester to challenge him directly, arguing that a “useless” organ would be equally inclined to grow or diminish, and that panmixia could not account for reduction unless smaller size itself conferred an advantage. The exchange extended over eight weeks in Nature’s pages, with Romanes refusing to concede and instead insisting that Lankester fundamentally misunderstood his position.

By the close of the century, such exchanges had become familiar features of Nature’s pages. The lay reader had largely left Nature, which now served primarily as a medium for the scientific community. Prominent figures continued to contribute at rates often exceeding the prior generation and demonstrated an increased willingness to position Nature at the center of British scientific discourse.

Entering the 20th Century

For all its growing influence, Nature wasn’t yet particularly prestigious. It lacked the rigor of journals like Annalen der Physik or the Philosophical Transactions of the Royal Society, finding survival through patronage and speed.2 At this time, Richard Gregory, an administrator rather than a practicing scientist, was hired as Nature’s editor-in-chief in 1919 — a smart choice given that many of Nature’s challenges were operational rather than scientific.

Sensible of his own limitations, Gregory had positioned himself not as a “man of science,” but as a “spokesman of science.” As a spokesman, Gregory was oriented more towards advocacy and would extend such efforts beyond Britain, positioning Nature as an international venue protecting scientific freedoms.

Starting in 1933, for example, Nature began criticizing the Nazi regime for their expulsions of Jewish scientists. The Nazi regime banned the journal from German libraries in 1937. Gregory later defended this position forcefully, arguing that only “a German political official” would expect scientists to remain silent while respected colleagues were expelled “as the result of bitter racial prejudice.”

By taking such a principled stance, Gregory established Nature as a venue where scientific merit transcended national interests, drawing cutting-edge researchers from around the world and elevating the journal’s international profile. Perhaps their most significant international contributor was the physicist Ernest Rutherford, a New Zealand-born physicist and Nobel laureate whose work on radioactivity was reshaping atomic theory. Rutherford benefited greatly from Nature’s rapid publication schedule to announce discoveries from his laboratories in Montreal and later Cambridge. His explicit use of Nature to “keep in the race,” particularly after being “scooped” by the Curies in 1899, captured a shift where speed of communication was becoming essential to participate in cutting-edge research.

This pattern made Nature unusual among prominent journals: domestic contributions steadily declined over time. By 1933, half of Nature’s letters came from outside Britain. By contrast, Science remained predominantly American even later in the century (by 1980, only 15 percent of its experimental content came from abroad). In making Nature international when most other journals remained domestic, Gregory had established what would become a keystone of Nature’s future prestige.

Yet progress was fragile, with the international vision waning under Gregory’s successors, A.J.V Gale and Lionel “Jack” Brimble. Viewing their role as publishing “as many credible scientific papers — particularly ones from respectable British laboratories — as possible,” editorial selections became more domestic as English was displacing German and French as science’s lingua franca.

That said, their passive editorial approach meant they largely accommodated, rather than restricted, international submissions. By 1965, nearly 60 percent3 of all articles and letters originated from abroad. This shift was largely contributor-driven, as scientists worldwide continued to see Nature’s utility for gaining visibility and establishing priority findings.

Adopting such a hands-off approach had consequences for editorial quality, however. Nature developed a reputation for printing almost anything that wasn’t demonstrably wrong, with editorial decisions often relying disproportionately on institutional prestige as a filter. One notable editorial misjudgment was the geophysicist Lawrence Morley’s seafloor spreading hypothesis, submitted from Canada in February 1963, which was dismissed by Nature’s referee as mere “talk at cocktail parties.” Seven months later, Vine and Matthew’s virtually identical hypothesis, bearing Cambridge credentials, sailed through to publication in what became known, with belated justice, as the Vine-Matthews-Morley hypothesis.

Still not considered a particularly prestigious journal by the mid-1960s, Nature suffered from mediocre output, erratic refereeing, and publication delays that exceeded 14 months, eroding the speed that had once been one of its strongest competitive advantages.4 As geologist Drummond Matthews (of Vine-Matthews-Morley fame) would later recall, Nature “dropped into a sort of vacuum … American labs wouldn’t hear anything of it — thought it was all nonsense.”

Yet, Nature’s position within Britain’s scientific establishment still attracted significant breakthroughs, particularly in biological sciences, where the editors had actual expertise. Perhaps most famously, Watson and Crick’s 1953 DNA structure paper was accepted within three weeks, without external peer review, after Physics Nobel Laureate Lawrence Bragg sent a “strong covering letter” to the editors, whom he knew personally.5

With a reputation resting less on systematic editorial excellence and more on adjacency to transformative figures, Nature was — confusingly — both a second-tier outlet and a site for breakthroughs that reshaped entire fields.

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The Turning Point

Gifted this unhappy inheritance in 1966, editor John Maddox set about transforming Nature from survivor to standard-bearer, confronting a publication backlog of six months or more — nearly 2,000 manuscripts — left behind by Brimble and Gale’s passive editorial approach. He would first restore the submission processing speed that had deteriorated under his predecessors, pursuing a more assertive editorial strategy, and laying the foundation for the selectivity that would come to define Nature’s modern identity.

To speed up article processing, Maddox imposed discipline: instituting daily editorial meetings and introducing a streamlined index-card tracking system6 that sped up publication. By December 1966, he was even printing submission dates to signal the journal’s restored speed.7

Perhaps the greatest departure from previous editorships was Maddox’s view that Nature was engaged in direct competition with other journals. Maddox pursued an editorial strategy that actively courted laboratory submissions, sometimes convincing authors to withdraw their manuscripts from rival periodicals.8 By courting higher-quality submissions and publishing them quickly, Maddox restored much of Nature’s reputation. This success did, however, create an issue: rising submissions overwhelmed the journal.

By default, this made Nature more exclusive. Maddox, for his part, didn’t necessarily want this; he was more interested in breaking news and saw gatekeeping more as a means to that end. So he attempted to implement a three-journal solution, splitting the original journal into Nature, Nature New Biology, and Nature Physical Science in 1971. The plan reflected Maddox’s journalistic instincts: print more papers, publish more frequently, move faster, perhaps even toward a “daily Nature” that functioned like a scientific newspaper.

Unfortunately for Maddox, this backfired. Authors in the satellite journals felt “demoted to the second division,” while British researchers appeared disproportionately in the flagship (over 50 percent) compared to the satellites (~33 percent), reinforcing perceptions of Nature as a “very British establishment journal.” When Nature recorded a financial loss at the end of 1972, Maddox was replaced.9

In 1973, Nature’s new editor, David Davies, scrapped the three-journal plan, returning to a single title while retaining Maddox's operational improvements. With submissions continuing to grow but channeled through one outlet rather than three, Nature rejection rates continued to rise. Authors sought out Nature not only for visibility but for the symbolic capital it conferred. For the aspiring scientist navigating an environment where funding had slowed and, in many fields, shrunk, publication in Nature represented a form of career insurance.

However, exclusivity was an asset only if it was perceived as legitimate. Davies set out to reform the editorial process, moving it from the insular circles that had characterized earlier periods.

Within the first year of his editorship, Davies made peer review a requirement. Nature was late to this practice — American journals had been experimenting with peer review since the 1940s, and institutionalizing it since the 1960s — but the timing proved strategically important: U.S. academic departments increasingly demanded peer-reviewed publications for tenure decisions.

Ultimately, peer review didn’t transform Nature’s standing so much as protect it, converting exclusivity that might have seemed arbitrary into gatekeeping that appeared meritocratic.

Together, Davies and Maddox had directed a significant transformation. By the late 1970s, they had created the essential architecture of modern Nature — a highly selective, internationally oriented, generalist publication. This architecture allowed Nature publications to function as Schelling points,10 coordinating attention and providing shared references that researchers across disciplines could build on without extensive explanation. Nature’s prestige, in other words, derived less from gatekeeping quality than from solving a coordination problem.

And by solving that problem, Nature became valuable as career insurance. Publication in Nature provided a universally recognized signal for hiring committees, grant reviewers, and colleagues. It also had scientific value, because breakthroughs often arise when researchers apply principles from their own discipline to another. A paper’s inclusion alongside others of unrelated inquiry thereby indicated that a scientist’s work wasn’t only impactful in their own field but contributed to science on the whole.

Davies, who believed that staying in the same role too long led to personal stagnation, left Nature in 1980. To the surprise of many, including Davies, he was to be replaced by a returning Maddox, whose reappointment was facilitated by management changes at Macmillan, particularly the declining influence of one of its publishing executives, Jenny Hughes, who had orchestrated his prior exit.

Upon returning, Maddox set out to establish Nature as the definitive publication for the international scientific community. By 1980, four-fifths of articles and letters already originated from outside Britain. Nature extended this reach by opening offices in Tokyo, Paris, Munich, and Hong Kong. International expansion was accompanied by increased selectivity. By the late 1980s, Nature’s acceptance rate had fallen to just 12.5 percent (down from 35 percent in 1974), making publication more highly coveted; for comparison, editor Daniel Koshland Jr. reported Science’s acceptance rate at approximately 20 percent in 1985.

Throughout both editorships, Maddox had maintained a conviction that a scientific journal “should have an opinion on the state of science,” rather than serving as a passive conduit. During his first tenure, Maddox had personally taken over writing editorials, often at the last minute, to keep them current and provocative, and restructured the journal to place news and opinion prominently at the front. His second tenure would see a more direct approach, albeit sometimes controversially, such as when he personally investigated claims about homeopathy in 1988, drawing criticism for creating a “circus” atmosphere, and again when he deployed editorial skepticism against cold fusion claims the following year.

Despite such blips, by 1995, Nature had largely solidified its position through its core strengths. Its selectivity made publication valued across the global scientific community. Its international reach connected researchers. Finally, its approval had become one of science’s most valued forms of validation.

Nature in the New Millennium

Upon assuming the editorship in 1995, Philip Campbell — a physicist who had spent the previous decade in science publishing, including as founding editor of the magazine Physics World — was tasked with preserving the legacy of Davies and Maddox as the journal transitioned from print to pixel. Through editorial independence, digital presence, and selective competitive engagement, Nature would continue to strengthen its institutional position.

Institutional security, however, often rested on foundations beyond Campbell’s direct editorial control. During Campbell’s editorship, Nature’s portfolio expanded significantly: though sub-journals had resumed under Maddox with Nature Genetics in 1992, Campbell’s tenure would see them increase in number from 3 in 1995, to 30 by 2018, with many more partner journals.11

Campbell and other editors proposed or were consulted about new journal content; in the 2010s, he recalls supporting the initiation and early development of multidisciplinary thematic journals such as Nature Climate Change and Nature Sustainability. This devolved authority operated across multiple levels: issue-by-issue editorial decisions remained independent from corporate strategy, the journal and magazine maintained independence from one another, and individual Nature-branded journals operated independently from the flagship.12

Another significant development during Campbell’s tenure was the digitization of Nature content. Just as Davies had protected Nature’s standing through peer review — not by implementing it brilliantly, but by ensuring its absence couldn’t be used against the journal — digitization served a similar defensive function. Even though nature.com launched inauspiciously in 1995, with limited content, technical issues, and no full papers, its existence mattered more than its execution. This imperfect step, taken to be seen as modern and avoid anachronism, would prove foundational as scientific communication moved overwhelmingly online.

Campbell’s control was primarily editorial; for example, he sought to boost Nature’s attention to research themes he felt were undersupported, expanding coverage of foundational themes like methodology and scientific integrity, as well as specific subject matter such as marine science and mental health. Campbell also initiated greater engagement with the social sciences across Nature’s magazine and journal content, which underpinned the subsequent expansion of multidisciplinary research in Nature and its thematic journals beyond the natural sciences.

Editorial independence remained important, even when at odds with the publisher’s interests. One example of this independence was the Human Genome Project, an international project to sequence, map, and identify all human DNA. In 2000, Craig Venter’s Celera Genomics and the public Human Genome Project were completing their sequences, with Science pursuing both manuscripts. Venter insisted that some data remain behind a paywall (a position not considered heretical at the time). Campbell, however, refused these terms, judging it more important that data published in Nature remain publicly accessible, even at the risk of losing both sequences to Science. Venter did indeed go to Science, though Nature was able to publish the public project.

Similarly, when DORA (the Declaration on Research Assessment; an initiative advocating for the evaluation of research on its own merits rather than relying on journal metrics) launched in 2012, Nature abandoned a marketing campaign that had highlighted impact factor as a way to boost subscriptions. Campbell had been a longstanding critic of impact factor, though Nature had continued employing the metric in its marketing. Their public endorsement of DORA, however, cast this reversal as a matter of principle, giving Nature reputational capital for championing fairer evaluation practices. While this action carried some cost in absolute terms (abandoning a successful marketing lever isn’t nothing) Nature’s market position made this cost bearable, whereas it would have been prohibitive for a less established journal.

Perhaps most unusual about Campbell was that he approached rivalry selectively. He was seemingly indifferent to ordinary competition, but would pursue landmark contests intensely. “I can honestly say that we spent little time looking at what other journals were doing,” he would later muse.13 But when the symbolic value justified a more intensive pursuit, such as the Genome Project, Nature would compete aggressively. Otherwise, Campbell operated with a “room for both” philosophy regarding Science, seeing each journal as serving its own constituency. This selective engagement reveals that Nature’s strength during this period came not from controlling everything, but from knowing what mattered for preserving its position.

Modern Nature

When Magdalena Skipper, the current editor-in-chief, succeeded Campbell in 2018, she commanded a journal whose reach and influence surpassed anything her predecessors had inherited. Yet the surrounding scientific ecosystem was also far less stable. Preprints had matured through platforms like bioRxiv and arXiv, the open science movement was gathering momentum with initiatives like Plan S14 and platforms such as PLOS ONE,15 and conventional scientific institutions faced mounting scrutiny.

Where Campbell had practiced selective indifference to competition, Skipper brought a different sensibility, actively monitoring rivals. Attentiveness to competition extended beyond traditional academic journals to include outlets such as The Guardian and Financial Times, all competing for mainstream public attention on scientific developments, particularly during the pandemic. Although Nature held scientific authority, these mainstream outlets commanded greater public reach.

While Nature cannot beat these publishing giants on reach, Skipper’s ambition to foster “true multidisciplinarity” does extend its breadth. Throughout history, she observes, Nature has been “multidisciplinary primarily within the natural sciences.” Under Skipper, the journal has expanded into physical sciences, clinical research, social sciences, and engineering. Skipper’s guiding idea is that today’s most pressing questions demand collaboration across fields: “innovation often comes with an element of social sciences,” she says.16

Widening the lens, however, doesn’t mean capturing everything. Skipper advocates for an “ecosystem with different publishing approaches: inclusive and selective.” Not everything requires Nature-level selectivity; there is value in venues for replication, negative results, and less conventionally interesting datasets. Publishing, she contends, is inseparable from research itself: “not thinking about publication when conducting research is a conceptual error,” as research without dissemination has limited value.

For the critic of scientific publishing, however, it’s the journal itself, no matter how inclusive or reformed, that is the problem. In June 2025, Astera Institute, a nonprofit research organization, announced it would no longer fund traditional journal publications. For Astera, the journal system has flaws so deeply entrenched that they resist reform: publications become final stamps of approval with mistakes rarely corrected, artificial scarcity fuels competition over collaboration, and articles don’t adapt as new evidence emerges, allowing flawed studies to mislead fields for decades.17

While quite the indictment, there is merit to many of these complaints. As such, there are reforms that journals can implement that attempt to redress them. One especially illustrative example (although there are others) is retraction. Skipper considers it in Nature’s interest to “clean up [its] own pages.” She views retractions as visible evidence of vigilance rather than hidden embarrassment. Indeed, Springer Nature18 retracted 2,923 papers in 2024, with 61.5 percent addressing historical papers published before January 2023 as part of what the company describes as its commitment to “cleaning up the academic record.”

That said, these retraction efforts are not as thorough as they sound. This is because the complexity of removal processes and procedural requirements can override editorial judgment and stifle effectiveness. For example, in December 2016, independent researchers published an investigation uncovering nearly 300 fraudulent papers by two Japanese physicians, Yoshihiro Sato and Jun Iwamoto, across 78 journals. Among the publishers implicated was Springer Nature, which (as of 2024) had only retracted 13 of the 45 Sato-Iwamoto papers it had published.

Arguably more troubling was that at the Journal of Bone and Mineral Metabolism (a Springer Nature journal), only one of eleven papers was retracted, despite the editors recommending withdrawal, because the institutional investigation remained incomplete. Although the intention to reform may be sincere, procedural dependencies can override editorial judgment.19

Unlike her predecessors, who established Nature as the central hub for international science, Skipper must now defend that position against emerging alternatives in a maturing ecosystem of preprints, open access mandates, and funder defection. What her predecessors could largely take for granted — that a selective, central venue served science well — is itself contested.

Ultimately, the question isn’t so much whether Nature deserves its prestige (history shows that much of its success has been circumstantial and opportunistic rather than meritorious) but whether the coordination function it now serves is sufficiently valuable to the scientific ecosystem.

After all, in building its prestige, Nature became a vehicle for features that make scientific ecosystems function: international collaboration, multidisciplinarity, rigor and evaluation, and reach. Prestige may connote selectivity, but it speaks more to the broader question of what science is valuable and, as history demonstrates, that question was never answered by merit alone. Elite networks and well-endowed institutions may have shaped Nature’s ascension, but we should not mistake the system that emerged for one that reliably surfaces the best work.

Prestige journals became a default filter, but even that may be fragmenting. As submissions outpace what peer review can absorb, prestige risks becoming a marker of scarcity rather than quality, while scientific discourse migrates to faster venues. Yet coordination without quality control is insufficient. Not all science is equally valuable, and not all scientists have the same amount of integrity. In the era of paper mills, AI slop, and epistemic pollution, whatever system comes next — whether prestige journals or something else entirely — must contend with how to navigate this noise. We have seen one way to do this and understand how we arrived there. We may well need another.

Robert Reason is a Parliamentary Researcher. His prior academic work includes research on economics, metascience, and political misinformation.

Thanks to Melinda Baldwin for her foundational book, Making Nature: The History of a Scientific Journal, and her time in discussion, and to Philip Campbell and Magdalena Skipper for their generous and insightful interviews. These interviews heavily inform the sections about their editorships. Header image by Ella Watkins-Dulaney.

Cite: Reason, R. “How Nature Became a ‘Prestige’ Journal.” Asimov Press (2026). https://doi.org/10.62211/27hq-98kj

By Michael DePeau-Wilson

For millennia, our ancestors sought every imaginable cure for the common cold, from ancient Greeks who boiled hyssop with figs, water, honey, and rue, to the 15th-century English, who made a remedy by brewing “stale ale, mustard seeds, and ground nutmeg.”

Despite such efforts, generation after generation continued to suffer from nasal congestion without any effective, scientifically proven alternatives.

This began to change around the turn of the 20th century with the rise of industrial chemistry. Whereas ancient people used boiled herbs, ground botanicals, and bloodletting to relieve cold symptoms, improved chemical synthesis methods allowed for the creation of a much neater and more precise “commodity-based medicine,” characterized by pills and powders.

Oral phenylephrine was one such chemical treatment. It was first synthesized in 1927 by the German chemist Helmut Legerlotz, who sought to replicate the hormone epinephrine (more commonly known as adrenaline), which stimulates receptors connected to blood vessels, causing them to narrow. The formulation that would become phenylephrine was closely related to this hormone and was purported to affect blood vessels in the nose, shrinking swollen mucus membranes and opening the airway.

By 1938, pharmaceutical products company Frederick Stearns & Company had begun to sell phenylephrine to millions of Americans under the brand name Neo-Synephrine. It was initially sold as a liquid solution, taken orally or intranasally, for the treatment of “the common cold.” In some cases, physicians also used phenylephrine to manage hypotension caused by neuraxial anesthesia during pregnancy or as an eye treatment. And by the 1950s, it was being offered in tablet form, similar to modern formulations.

In the early 1970s, however, the FDA re-examined phenylephrine as part of a massive effort to review all older prescription drugs — more than 3,400 that had been approved based only on safety data between 1938 and 1962 — for proof of effectiveness, a process instated after the thalidomide crisis. A panel of experts evaluated fourteen studies of oral phenylephrine, most of which had been funded by its manufacturer, Sterling-Winthrop. Only a few of those studies had shown any benefit, and several others found the drug performed no better than a placebo in relieving nasal congestion.

Despite this tepid evidence for phenylephrine’s efficacy, however, the panel deemed the drug “safe and effective,” and it remained on the market for another 50 years. It was not until November 2024 that the FDA announced plans to revoke approval of oral phenylephrine as an active ingredient in over-the-counter (OTC) cold medications used for nasal decongestion.

But why did it take half a century for the FDA to pull an ineffective drug from the market?

While one could read the sluggish pace of the FDA as an exercise in caution, details of this saga reveal other explanations for the agency’s often slow drug removal process; most notably, its interdependence on industry-sponsored data and funding for drug reviews and its tendency to quickly act on safety concerns, while dragging its feet when it comes to those of efficacy.

The problems this dynamic produces are manifold. First, even though phenylephrine didn’t directly cause any deaths, every drug carries some level of risk for side effects, and this risk–benefit equation collapses when a drug is not effective.1 Second, common generic drugs represent billions in revenue for pharmaceutical companies (and millions in fees paid to the FDA), even when their therapeutic worth is dubious. When such drugs continue to generate large profits without offering substantive benefits, they linger on the market longer than they should. And finally, without sufficient resources and scrutiny devoted to generic and monograph drug products after their initial approval, drugs like phenylephrine often remain widely used long after their efficacy has been discredited.

To understand the story of oral phenylephrine and why its removal took 50 years, we must first examine the forces that shaped the FDA itself.

The Origins of Drug Regulation

Oral phenylephrine emerged during a highly productive period in medicine. In 1922, Leonard Thompson, a 14-year-old boy with diabetes, became the first person to be treated with insulin injections. In 1928, Sir Alexander Fleming discovered penicillin in mold growing on one of his bacterial samples. And in 1937, Max Theiler, a South African-American physician, developed the first vaccine for Yellow Fever.2 As the scientific breakthroughs quickened, legislators struggled to keep pace.3

A 1937 tragedy finally impelled the federal government to impose regulations on the growing drug market. A Tennessee company, S. E. Massengill, had released a medicine called Elixir Sulfanilamide, a raspberry-flavored liquid version of an antibiotic (sulfa) used to treat strep throat and other infections. To dissolve the medicine, the company’s chemists had mixed it with diethylene glycol, a toxic chemical used in antifreeze. They did not run any safety studies on this updated mixture, as none were required at the time.

Within weeks, this Elixir syrup had caused the death of more than a hundred people across fifteen states, many of them children. The disaster provoked national outrage and congressional hearings; newspapers printed photographs of the victims, and the elixir was pilloried on the Senate floor. This anger spurred the Federal Food, Drug, and Cosmetic Act of 1938, which, for the first time, required manufacturers to prove that their products were safe before sale. Oral phenylephrine entered the market that very year, riding the tide of modern, chemistry-based medicine and the first wave of genuine pharmaceutical oversight in American history.

After the 1938 Act, however, it would take another 24 years before the government would introduce requirements for drug efficacy. This time, the policy changes were driven by a narrowly averted disaster.

In 1961, Chemie Grünenthal, a German-based company, asked for U.S. approval to sell thalidomide, a sedative that physicians abroad were prescribing to ease morning sickness in pregnancy. Its American partner, Richardson-Merrell, submitted a file typical of the pre-1962 era: brief animal-toxicity studies, physician testimonials from Europe, and anecdotal “clinical experience” reports. There were, however, no controlled human trials, no data on how the drug was metabolized, and no tests of its effects on fetal development.

The FDA reviewer assigned to the case, Frances Oldham Kelsey, vehemently interrogated Richardson-Merrell’s claims. Reports from Europe had already described cases of peripheral neuritis (nerve damage and tingling) in patients taking thalidomide, findings the company had not disclosed.4 Kelsey also noted that the safety file contained nothing addressing use in pregnancy, even though the drug was aimed at pregnant women.

Kelsey refused the application for thalidomide, asking for more evidence. Shortly after, she saw a case report published in the British Medical Journal linking thalidomide to catastrophic birth defects. Her vigilance mostly kept the drug away from Americans (although by 1962, unregulated trials for the drug were believed to have exposed roughly 20,000 Americans to thalidomide). Abroad, where the drug had already been approved, more than 10,000 children were born with limb deformities.

The thalidomide disaster sparked a public outcry for stricter regulations in the FDA’s drug review process. So in 1962, Congress passed the Kefauver-Harris Drug Amendments to the Food, Drug, and Cosmetic Act of 1938. For the first time, these amendments required pharmaceutical companies to prove both the safety and efficacy of new drugs through well-controlled clinical trials before FDA approval. Pharmaceutical companies seeking to release new products were required to be evaluated on a case-by-case basis, according to the New Drug Application (NDA) process.

Importantly, the Kefauver-Harris Drug Amendments were also retrospective. That is, the FDA was required to go back and assess or reassess the thousands of drugs, including prescription and OTC drugs, that had long been on the market. To manage the enormous workload, the agency created the Drug Efficacy Study Implementation program in 1966, partnering with the National Academy of Sciences to review every prescription drug approved since 1938.

Because OTC drugs were considered safer, however, they were given a lower priority than prescription medications and would be reviewed last. By 1972, the FDA still had only examined a fraction of OTC products already on the U.S. market. To expedite this monumental task, the agency developed a new process for assessing and approving large groups of OTC drugs using an internal rulemaking protocol. The new protocol created the OTC Drug Monographs program, which would manage the review of up to half a million OTC drugs and was one of the largest and most complex regulatory undertakings in the agency’s history.

This process allowed the agency to review an entire category of drugs for a specific type of drug product, such as cold medication. The ingredients and instructions for use, like dosage and warnings deemed acceptable for each specific product type, were added to an approved list, called a monograph. It was essentially a shortcut, for even as its budget grew, the FDA simply did not have the resources to review each formerly approved drug individually.

With the OTC Drug Monograph program, a pharmaceutical company looking to sell an OTC drug didn’t need to submit its own application for FDA approval. Instead, it only needed to ensure that its product fell within the conditions laid out in the relevant OTC monograph — using an ingredient that the FDA has already deemed generally recognized as safe and effective (GRASE), at the approved strength (e.g. 10mg), dosage form (e.g. oral tablet), and labeling. Once those standards had been met, the company could market the product immediately, as compliance with the monograph itself serves as legal authorization to sell it. It is only when a product falls outside an existing monograph — say, because of a new active ingredient, higher dose, or new indication — that a manufacturer has to go through the more rigorous NDA process, either as a generic or a new brand-name drug product.

Around the time that these two pathways to approval were forming, the FDA budget also doubled, and it gained regulatory power over a wider swath of the medical industry. By 1976, the agency added four new bureaus overseeing biologics, radiological health, medical devices, and toxicological research. The FDA hardly resembled the agency that had given oral phenylephrine its safety approval 34 years before. But its monograph process and other efforts to streamline drug review processes would have a profound influence on its future.

Structural Flaws

Oral phenylephrine was reviewed under the Cold, Cough, Allergy, Bronchodilator, and Antiasthmatic (CCABA) OTC monograph. From 1972 to 1976, a nine-member advisory panel reviewed data from 14 studies conducted between 1959 and 1975. Of those 14 studies, 12 assessed phenylephrine’s efficacy and seven showed positive results. But the vast majority of those studies also came from a single sponsor (the company seeking approval) — Sterling-Winthrop Research Institute, a company heavily invested in phenylephrine’s success.5

The FDA’s dependence on company-funded research is not new. It dates back to the original structure of its drug review process, which relies on the sponsor to provide evidence that a product is safe and effective. While it makes sense that the applicant should fund this research, it is perhaps too much to expect that the same company would be unbiased enough to produce reasons why the product should not be approved.

Sterling-Winthrop had purchased the original manufacturer of oral phenylephrine products, Frederick Stearns & Company, in the 1940s and was still producing Neo-Synephrine when the committee met. Thus, of the seven studies that showed positive efficacy results for oral phenylephrine, six had been conducted by Sterling-Winthrop.

In 1976, after years of review, the advisory panel determined that oral phenylephrine was “safe and effective as an oral and as a topical nasal decongestant for OTC use.” The agency’s commissioner accepted this finding and eventually granted phenylephrine tentative approval in 1985. Despite this approval, the 1985 advisory committee admitted the data was “not strongly indicative of efficacy” for oral phenylephrine, according to the FDA briefing documents released in 2023. Still, by 1994, oral phenylephrine had been granted final inclusion in the cold-medicine monograph.6

Oral phenylephrine’s inclusion (despite lukewarm evidence on efficacy) was made possible by a couple key elements within the review process. First, oral phenylephrine was being considered alongside dozens of other drugs within its category (and thousands of generic drugs in total), which stretched the capacity of the reviewers. And second, the studies presented to the original advisory panel were not subjected to any third-party review.

Today, the FDA has evolved its drug review processes to include more requirements — such as publishing guidelines for optimal drug study designs, overseeing study sites and conduct, and requiring preapproval for study protocols. But the agency still relies heavily on industry-sponsored evidence, without requiring any third-party review of those outcomes, including from its Advisory Committees. And in the decades since phenylephrine’s approval, Congress has further intertwined the FDA’s budget with the pharmaceutical companies it seeks to regulate through “user fee” programs.

These fees are mandatory payments that pharmaceutical companies make to the FDA to help fund the agency’s drug review and oversight activities. Established by Congress through a series of laws beginning with the Prescription Drug User Fee Act (PDUFA) of 1992, they were meant to speed up drug approvals by giving the FDA resources to hire staff and meet review deadlines.

Companies pay fees both when submitting new drug applications — roughly $4.3 million per application in 2025 — and annually to maintain products that have already been approved. Similar fee programs exist for generic medicines under the Generic Drug User Fee Act (GDUFA), and for over-the-counter monograph drugs, and those payments are used to support applications, facility inspections, and drug product reviews. By 2022, user fees represented 46 percent of the agency’s total budget, or nearly $3 billion.

Taken together, the monograph rule of 1972 and the PDUFA of 1992 propelled the FDA toward an era of shorter review periods and faster drug approvals. Further efforts to expedite approvals came in 1997 when the U.S. Congress passed the Food and Drug Administration Modernization Act, which codified the agency’s accelerated approval program and allowed the agency to approve drugs based on surrogate endpoints while waiting for confirmatory clinical trials. (An example of surrogate data would be evidence of a cancer drug’s reducing the size of a tumor in a patient. While it’s not hard to see why this measure is promising, it does not demonstrate how well the drug would treat a patient’s overall condition, or for how long.)

The median number of generic drugs approved each year increased from 284 between 1985 and 2012 (when the GDUFA went into effect) to 588 between 2013 and 2018. For New Drug Applications, the average number of annual approvals increased from 34 in the 1990s to 42 in the mid-2010s.

There are also signs that the agency would like to shorten approval times further still. In June 2025, Commissioner Marty Makary announced plans to reduce the average review period for certain drugs deemed in “the health interests of Americans” from an average of 10 months to just one.7

While faster approvals are a good thing in that they speed up access to potentially lifesaving treatments, they can also, on occasion, mean drugs with poor efficacy go overlooked, especially if the FDA is relying on more surrogate endpoints and less thoroughly reviewed data.

In one example, the FDA granted Roche an accelerated approval in March 2019 to market the monoclonal antibody atezolizumab in combination with a chemotherapy drug for the treatment of triple-negative breast cancer. The decision was based on early results from a phase 3 clinical trial on atezolizumab but was also made contingent on the full results of a separate phase 3 trial. When the results of the second trial were made available in 2021, they proved disappointing, resulting in the FDA ordering its removal from the market.8

Notably, this removal illustrated a rare example of the accelerated system working properly, but there are many other occasions when a company fails to conduct the confirmatory trial, allowing ineffective drugs to remain on the market. This issue becomes more concerning when factoring in the number of drugs that never meet those confirmatory trial standards at all. In fact, between 2009 and 2022, nearly a quarter of approved cancer drugs were withdrawn due to a lack of benefit over standard of care, according to a 2023 JAMA research letter.

Additionally, more than half of newly approved pharmaceutical products between 1980 and 2022 secured approval by using at least one of the FDA’s expedited designations, according to a 2024 Nature study. The study also notes that of the drugs submitted and approved via accelerated means since 1992, 11.4 percent were based on surrogate endpoints. Indeed, the authors of the 2024 Nature study concluded that “the approval of new drugs without reliable confirmatory evidence of their safety and effectiveness transfers the burden of the decision about the risk-benefit trade-off to clinicians and patients.”

Trying (and Failing) to Pull a Drug

After oral phenylephrine was added to the OTC monograph in the 1970s, it receded quietly back into the medicine cabinets of Americans for decades. Throughout the 1980s and 1990s, consumers around the U.S. had plenty of choices to alleviate their cold symptoms, including the decongestant drugs phenylpropanolamine and pseudoephedrine, sold as Sudafed.

However, this uneventful period did not last. Starting in 2000, the FDA became aware of concerning safety data related to phenylpropanolamine.9 A group of Yale researchers found a link between the decongestant and increased risk of hemorrhagic stroke in women. The FDA acted swiftly, removing it from the OTC monograph and asking drug manufacturers to reformulate any products containing it.

Then, in 2005, political pressure forced Congress to take action by implementing additional safety measures regarding pseudoephedrine, without input from the FDA. At the time, the U.S. was at the height of the methamphetamine epidemic, and pseudoephedrine was an ingredient commonly used to cook meth. Congress responded by passing the Combat Methamphetamine Epidemic Act of 2005, which removed pseudoephedrine from the OTC monograph and required it to be sold behind the counter.

In a span of just five years, oral phenylephrine went from being one cold medicine on a crowded pharmacy shelf to the primary ingredient in many OTC decongestants. While it was part of the same OTC monograph approval process as phenylpropanolamine and pseudoephedrine, phenylephrine did not raise any safety concerns (and it was not used to cook meth.) Its approval status remained unchanged, and common cold medicines, like Sudafed, were reformulated with it, becoming “Sudafed PE.”

As pharmacists and consumers turned to these reformulated drugs, however, they noticed a difference from the old pseudoephedrine-based products; namely, that they were not as effective at reducing cold symptoms. This moment marked the beginning of the fall of oral phenylephrine.

In 2005, retail pharmacists across the country began hearing from patients that Sudafed PE did not work like the “old” Sudafed. When Randy C. Hatton, pharmacist at the University of Florida, caught wind of this, he began looking for answers.

He soon came across data, published by a pharmacist named Leslie Hendeles in 1993, showing that oral phenylephrine was not as effective as its recently dethroned counterparts, phenylpropanolamine and pseudoephedrine. Concerned about the drug’s approval, given the poor evidence for its efficacy, Hatton and Hendeles began to collaborate. Since several studies from the 1960s and 1970s remained unpublished, they had to submit a Freedom of Information Act request for the FDA’s data on the drug’s initial approval before conducting a meta-analysis of the original research.

In 2007, the duo published a systematic review and meta-analysis that pooled data from randomized, placebo-controlled trials. They found that a 10 milligram dose of oral phenylephrine — the same dose recommended by the drug’s manufacturer — did not significantly reduce nasal airway resistance compared to placebo, and patient-reported symptom relief was inconsistent. Hatton and Hendeles also discovered that most of the positive studies the original 1976 panel had relied on were unpublished, manufacturer-sponsored, and lacked adequate controls.

To get the FDA to reconsider its approval of oral phenylephrine, Hatton and Hendeles filed a citizen petition. These petitions were made possible by an amendment made to the FDA in the 1970s, which allowed members of the public to request that the FDA “issue, amend, or revoke a regulation.”

Afterward, Hatton noted that the agency “somewhat begrudgingly convened a Nonprescription Drugs Advisory Committee meeting to review the compound’s effectiveness.” In that meeting, Hatton and Hendeles presented their findings that the standard 10 milligram oral dose of phenylephrine showed little or no consistent efficacy compared to placebo in reducing nasal congestion. They urged the FDA to revise its dosing criteria and go further: revoke OTC approval for children under age 12, citing the lack of safety or efficacy data for that age group (and no supporting pediatric trials).

Hatton and Hendeles also requested that the agency authorize and review higher doses — up to 25 milligrams every four hours — to test whether a stronger dose could overcome the drug’s poor oral absorption, which earlier data suggested might be a limiting factor.

In their 2007 petition, Hatton and Hendeles argued that the 1976 OTC panel had ignored dose-response evidence in selecting the 10 milligram dose. For example, the duo pointed out one study (not reviewed by the original panel) where a 25 milligram dose produced a statistically significant reduction in nasal airway resistance compared to 10-milligram or 15-milligram doses. Hatton and Hendeles also analyzed the evidence the 1976 panel cited and determined that only four studies truly supported phenylephrine’s effectiveness, while seven studies showed no benefit over placebo. “In our view,” they wrote, “the panel reached a specious conclusion that was not based on a systematic review of the available data.”10

Although their petition prompted a formal review, it was only the start of a long process. In December 2007, the FDA’s Nonprescription Drugs Advisory Committee reviewed the Hatton-Hendeles petition, hearing arguments from both researchers and industry representatives who defended phenylephrine’s 10-milligram dose.

The committee voted twice. It found, 11 to 1, that existing data suggested the 10-milligram dose might be effective, and 9 to 3 that more research was needed on higher doses. After the meeting, Schering-Plough, a subsidiary of Merck that presented data during the meeting, and McNeil Consumer Healthcare, the manufacturer of Sudafed PE, began testing those higher doses. Four clinical trials followed, the last two appearing in 2015.

That year, Hatton and Hendeles filed a second petition summarizing the new results, which showed that even quadrupling the dose to 40 milligrams produced no greater relief than placebo. Their first petition had asked the FDA to revoke approval for children under 12 and to re-evaluate dosing; this time, they demanded the FDA completely remove oral phenylephrine from over-the-counter decongestants.

They may have expected a swift response, as in 2007, but none came. Eight years later, in September 2023, the FDA finally reconvened its advisory committee; this time to decide whether to strike oral phenylephrine from the OTC monograph entirely.

This long wait is typical of the FDA’s citizen petition process. Petitioners must gather and analyze data, prepare legal filings, and present them for review, only often to be told that more evidence is needed. A 2016 rule requires the FDA to respond to petitions within 180 days, but the agency rarely meets that deadline. Indeed, a 2023 Health Law Advisor report found that many petitions, especially those submitted to the Center for Devices and Radiological Health, have gone unanswered for years or decades.

When the agency does respond, the results are not usually good for petitioners. Between 2008 and 2023, the FDA resolved 265 petitions: most were denied or withdrawn, 58 were partly granted, and only 10 succeeded, meaning the FDA agreed to make changes requested in those petitions.

Citizen petitions were devised to serve as a check on the agency’s mistakes, allowing outside scientists to challenge medicines that no longer meet modern standards of efficacy. While this particular petition eventually succeeded, the travails faced by Hatton and Hendeles raise the question of whether citizen petitions, as a mechanism by which drugs are challenged, are effective. Other than in the case of oral phenylephrine, only one other petition has helped prompt the FDA to remove an ineffective or unsafe drug since 2001.11

In fact, an independent analysis of the FDA’s response to citizen petitions found the agency denied “87.3 percent of petitions by individuals, not-for-profit organizations and advocacy groups, and other governmental agencies” between 2001 and 2013. The authors noted that even many partially granted petitions were effectively denials due to the agency’s refusal to act on the request. Following their review of nearly 2,000 petitions, they concluded that “citizen petitions filed by ‘ordinary’ citizens are rarely successful.”

Approvals Take Years, Removals Take Decades

From 2007 to 2015, Hatton and Hendeles had presented the FDA with several pieces of corroborating evidence that oral phenylephrine didn’t work. By the time the advisory committee reconvened in 2023, the decision seemed inevitable. One panelist even said further debate would be “beating a dead horse.”

Forty-seven years after phenylephrine’s first approval, the committee voted unanimously that the drug was ineffective. In its briefing documents, the FDA panel offered little explanation for the long delay, citing only that phenylephrine had no known safety issues and that removing it would have “a significant impact on industry.” (At the time of its removal, roughly half of U.S. households had purchased phenylephrine products over the previous year, amounting to $1.8 billion in sales.) Given this hit to the market, it’s perhaps unsurprising that this process was so protracted. Phenylephrine products were tremendously lucrative, and although they weren’t helping people, they weren’t harming them either.12

To illustrate this perspective, the chair of the 2007 nonprescription drugs advisory committee, Dr. Mary Tinetti, posited that efforts to remove the drug from the market were “ignoring the fact that millions and millions of people are using [oral phenylephrine products] and are voting with their pocketbook.” She added that “clearly, they feel that [oral phenylephrine products] are effective or they wouldn’t be using them.”13

The more charitable take, however, is not that the FDA is willing to overlook efficacy in favor of maintaining market stability, but simply that once drugs have been approved, it is onerous and expensive to revisit their qualifications. In fact, the agency was provided some reprieve from this predicament during the early days of the COVID-19 pandemic when Congress passed the Coronavirus Aid, Relief, and Economic Security (CARES) Act of 2020. The CARES Act reformed the OTC monograph process to make it “less burdensome on the agency to update and create new monographs.”

It’s likely not a coincidence that the agency finally reconvened the advisory committee to review oral phenylephrine shortly after the CARES Act went into effect.

The challenge ahead, then, is to make such reforms and corrections happen faster. And not only faster, but earlier in the process, as rapid approval and subsequent removal of those treatments would be destabilizing. What we need is not merely speed in both directions, but better vetting upfront and a smarter, swifter way to correct course when evidence changes.

This, of course, is no easy task. Every new law or rule change within the FDA joins the intricate scaffold propping up the weight of the entire U.S. drug market.

Lately, this scaffolding has come under enormous pressure from changes within the FDA, driven almost entirely by political ideologies. If the agency emerges from this moment intact, it will once again be time to consider the necessity of these changes to drug approvals and monitoring. However, if the agency cracks under the political pressures, future FDA leadership and the American people will have to find new ways to build this storied agency from the ground up all over again.

Even considering the precarity of the present moment, the FDA has been largely effective in balancing its commitments to both industry and consumers. When it comes to safety concerns, the agency has also been remarkably responsive to public pressure over the years, most notably in 1938 and in the 1960s. Its ability to adapt and improve has led to decades of relative stability while continuing to encourage drug innovation.

An example of this is the agency’s recent development of a proposed guidance statement outlining several rule changes to the accelerated approval process based on the Consolidated Appropriations Act of 2023. One of those changes requires drug companies to submit plans for confirmatory clinical trials before gaining approval, instead of waiting until after the approval to initiate trial planning. The guidance statement also requires drug companies to update the FDA on research progress every six months.

More crucially, this proposed statement also presented a new expedited withdrawal process for drugs approved through the accelerated pathway, paving the way to remove drugs that failed to match their nonclinical endpoints in clinical trials. Though a promising acknowledgment that the agency is aiming to respond more quickly to shortcomings, the changes have yet to be formalized.

Still, as the market for new brand-name drugs grows, the FDA needs to consider the downstream effects — 10, 20, or even 50 years in the future — for generic and OTC drug products. If the quality of new (and hastily approved) drugs wanes while they continue to stay on the market, it could lead to a glut of ineffective drugs clogging shelves and frustrating consumers in the not-so-distant future.

If the oral phenylephrine saga has shown us anything, it’s exactly how hard it can be to work backward. The agency shouldn’t focus all of its energy and resources on approvals if the process risks grandfathering in new drugs with comparatively fewer (and far more onerous) pathways to retirement. Instead, the agency needs to find pathways to remove ineffective drugs just as quickly and effortlessly as those that allow them to enter the market in the first place.

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Michael DePeau-Wilson is a health journalist whose work explores technology, medicine, clinical practice, and human behavior. Over a decade of professional reporting, he has covered a variety of medical specialties for national outlets including MedPage Today, Medscape, ABC News, and Anesthesiology News. His recent reporting on the rise of AI in healthcare and FDA regulatory updates reflects his broader focus on what happens when scientific progress meets the realities of clinical practice and patient care.

Thanks to Ben Gordon for feedback on this draft and Adam Kroetsch for providing an FDA insider perspective. Header Image by Ella-Watkins-Dulaney. Inspired by Leonard Karsakov’s 1941 U.S. Public Health Poster.

Cite: DePeau-Wilson, M. “Why the FDA Is Slow to Remove Drugs.” Asimov Press (2025). https://doi.org/10.62211/52fj-96ty

“I did not invent penicillin. Nature did that. I only discovered it by accident.”
—Alexander Fleming

Many know the story of Alexander Fleming’s chance discovery of penicillin. Fleming, a bit of an absent-minded professor (and a bit of a slob), left culture plates streaked with Staphylococcus on his lab bench while he went away on summer holiday. When he returned, he found that “a mould” had contaminated one of his plates, probably having floated in from an open window. Before discarding the plate, he noticed that, within a “ring of death” around the mold, the bacteria had disappeared. Something in the “mould juice” had killed the staphylococci.

Fleming immediately began investigating this strange new substance. He identified the mold as Penicillium rubrum and named the substance penicillin.1 He published his findings in the spring of 1929 in The British Journal of Experimental Pathology.2 But a decade later, pharmacologist Howard Florey and biochemist Ernst Chain at Oxford would pick up where Fleming left off. Alongside a USDA lab in Peoria, Illinois, the pair would develop penicillin into a life-saving drug and usher in the era of antibiotics.

This is the kind of science story everyone likes. One of serendipity and accidental discovery; a chance observation that changed the world. But is it true?

For decades, scientists and historians have puzzled over inconsistencies in Fleming’s story. For starters, the window to Fleming’s lab was rarely (if ever) left open, precisely to prevent the kind of contamination that supposedly led to penicillin’s discovery. Second, the story is strikingly similar to Fleming’s earlier discovery of lysozyme, another antibacterial substance, which also featured lucky contamination from an open window. Third, Fleming claimed to have discovered the historic culture plate on September 3^rd, but the first entry in his lab notebook isn’t dated until October 30^th, nearly two months later.

Last, and most important: penicillin only works if it’s present before the staphylococci. Fleming did not know it at the time, but penicillin interferes with bacterial cell wall synthesis, which only happens when bacteria are actively growing. Visible colonies, however, are composed mostly of mature or dead cells. By the time a colony can be seen, it is often too late for penicillin to have any effect. In fact, the Penicillium mold typically won’t even grow on a plate already filled with staphylococcus colonies. For years, scientists have attempted to replicate Fleming’s original discovery. All have met with failure.

Thus, it’s difficult to reconcile Fleming’s story with these historical and scientific discrepancies. Did he misremember events from 15 years earlier? Could he have fudged the details to make for a more compelling narrative? Or, might Fleming’s experiment have been subject to an unusual confluence of chance events unbeknownst even to him?

Speculation about how Fleming discovered penicillin is of little consequence compared to its practical impact. However, science is about evaluating evidence and moving closer to the “truth.” As we near the 100th anniversary of penicillin’s discovery — which undoubtedly will encourage even greater repetition of the story — it’s in this spirit that we must scrutinize the story’s veracity.

The historical and scientific data are limited and often contradictory. Nevertheless, several scientists and historians have worked hard to piece together what facts are certain and fill the gaps with their most probable guesses. The result is a range of competing theories, each attempting to explain what really happened in that St. Mary’s Hospital laboratory in the summer of 1928.

Fleming’s Account

The story of Fleming’s discovery of penicillin is primarily based on this passage from his 1929 paper:

While working with staphylococcus variants a number of culture-plates were set aside on the laboratory bench and examined from time to time. In the examinations these plates were necessarily exposed to the air and they became contaminated with various micro-organisms. It was noticed that around a large colony of a contaminating mould the staphylococcus colonies became transparent and were obviously undergoing lysis (see Fig. 1).

“Fig. 1” refers to a “Photograph of a culture-plate.” It shows separate, well-grown staphylococcus colonies around 2-4 mm in diameter spread across most of the plate’s surface. But on one edge, a large mold colony of about 20 mm in diameter, plus a secondary satellite colony, is clearly visible. This is labeled “Penicillium colony.” Surrounding it is a zone of about 20 mm in which the staphylococcus colonies are either not visible or have become semi-transparent ghosts. Those nearest to the mold are smaller than the rest, only 0.4 to 0.8 mm, while those towards the periphery are a bit larger, 0.8 to 1.7 mm. Fleming has labeled these “Staphylococci undergoing lysis.” Later, Fleming and his colleagues would claim that this was the original contaminated plate from which Penicillium was first isolated.

On its face, this seems simple enough. Everyone knows that penicillin destroys bacteria, and Fleming observed staphylococci seemingly being destroyed by a mold that produced penicillin.

However, upon closer reading of Fleming’s 1929 paper, it becomes clear that a great deal of work was either omitted or inadequately described. There is, for example, no description of the type of culture medium used; whether or not the plate had been incubated; how long it had been on the bench; and, most important of all, what species of Staphylococcus was being studied.

When publishing a scientific paper, scientists are expected to include a detailed description of their methods alongside their results. Like a recipe, these methods should clearly and comprehensively describe the materials used and the steps taken so that other scientists can replicate the experiment. And while incomplete or poorly-described methods are a perennial problem, the omission of these key experimental details (even in a report on an accidental discovery) is surprising.

This became a problem when, as interest in penicillin grew, other investigators tried to repeat Fleming’s discovery. In 1944, Margaret Jennings (who later married a long-time colleague and penicillin researcher, Howard Florey) spread purified penicillin onto plates of fully grown staphylococci. This should have had a more potent effect than Fleming’s pictured in Figure 1, which was allegedly produced only with the crude “mould juice” from an accidental contaminant. Jennings, however, observed no visible change.

In 1965, the pathologist W.D. Foster attempted a similar experiment using penicillin crystals dropped directly onto staphylococcus colonies, creating “astronomical” concentrations within their vicinity. But still, the colonies remained unaffected.

Other attempts at replication called into question whether the mold could have even grown on a plate full of staphylococci. Pharmacologist D.B. Colquhoun claimed that, in 1955, he found that Penicillium mold refused to grow on a plate already full of staphylococcus colonies. Or, that, if it did, it produced no visible effect on the colonies. He could, however, see an effect if the sequence of events was reversed: if the mold was allowed to grow for several days first, and the staphylococci was later inoculated onto the plate.

Although these failures are hard to reconcile with Fleming’s account, they are in line with what we now know about the biology of penicillin.

In 1940, the physician A.D. Gardner, researching alongside Florey, peered into his microscope to examine how penicillin affected individual bacterial cells. Surprisingly, adult cells seemed to be largely unaffected; however, when they divided, the young cells grew “as immense swollen filaments.” Like party balloons, they elongated and expanded, then popped.

“The morphological changes,” observed bacteriologist J.P. Duguid in 1946, “suggest that penicillin in these concentrations interferes specifically with the formation of the outer supporting cell wall, while otherwise allowing growth to proceed until the organism finally bursts its defective envelope and so undergoes lysis.” At the time, this was largely speculation. Not much was known about the biology of bacterial cell walls. But after a decade of study — motivated in no small part by a desire to understand how penicillin worked — this hypothesis has largely been proven correct.

The bacterial cell wall is a rigid, mesh-like structure composed primarily of peptidoglycan, a large macromolecule consisting of small subunits cross-linked by specialized enzymes called transpeptidases. The job of the cell wall is to maintain the cell’s shape and keep it from absorbing too much water. If the outward pressure from the cell’s contents becomes too great for the delicate cell membrane to contain, it bursts, spilling the cell’s innards. The cell wall, like a heavy-duty bicycle tire around a rubber inner tube, helps to resist this pressure, protecting the cell from mechanical stresses both inside and out.

Unlike a bike tire, however, cell walls need to be able to grow with the cells they enclose. To accommodate increasing cell size, bacteria are continuously breaking and rebuilding the peptidoglycan mesh. This is where penicillin comes in. Because penicillin has a similar chemical structure to a peptidoglycan subunit, it can bind to the transpeptidases that complete the final step in cell wall biosynthesis.3 When this happens, penicillin forms a covalent bond in the transpeptidase’s active site, irreversibly inactivating the enzyme. As it grows, the cell continues to disassemble its cell wall, but without the use of its transpeptidases, it can no longer rebuild it. Over time, the cell wall weakens and eventually bursts.

This explains why Jennings and others couldn’t replicate Fleming’s contaminated plate. A mature colony is mostly composed of adult or dead cells. These cells are unaffected by penicillin because they aren’t actively growing, and so aren’t actively breaking and rebuilding their cell wall. As a result, penicillin doesn’t cause mature cells to lyse, and the colony’s overall appearance doesn’t change. But if the penicillin is present before the staphylococci, it prevents the bacteria from growing and dividing, or they do so much more slowly. When that happens, they don’t form visible colonies. Thus, penicillin does not dissolve fully grown colonies, as Fleming had initially assumed, but inhibits their growth from the start.

The difficulty replicating Fleming’s discovery is frustrated by the ease with which it’s possible to “rediscover” penicillin by reversing the order of growth. By first growing Penicillium mold until it becomes a large colony, then seeding the plate with staphylococci, the result is indistinguishable from Fleming’s original plate. However, no trained scientist would intentionally use a culture plate visibly contaminated with a large mold — and certainly not an expert bacteriologist like Fleming.4

There are no contemporary records to corroborate the story that Fleming discovered the contaminated culture plate when he returned from holiday on September 3^rd: no lab notebook records, calendar notes, diary entries, or any letters. In the 1929 paper, the figure is simply labeled, “Photograph of a culture-plate.” The only evidence we have stems from recollections by Fleming and colleagues years later, after penicillin was recognized as a runaway clinical success. Fleming himself described the Figure 1 plate as the “original culture plate” in a 1944 paper. Yet, he also included the disclaimer that “after a lapse of fifteen years it is very difficult to say just what processes of thought were involved.”5

The earliest recorded mention of the mold and penicillin is an experiment written in Fleming’s lab notebook dated October 30^th, 1928 — nearly two months after he purportedly found the culture plate. Curiously, it does not describe the chance discovery of a contaminant, but a carefully constructed experiment that suggests Fleming had already spent some time isolating and characterizing the mold. In it, Fleming used the reversed-sequence culturing method: first, placing a mold spore on the plate and letting it grow into a large, penicillin-producing colony, then inoculating several pathogenic species of bacteria, including staphylococci, near the mold.

On October 30th, Fleming recorded the results: the mold affected a whole host of pathogens, including staphylococci, which could not grow near the mold. It’s a fine experiment, but it’s clearly not the discovery of an accidentally contaminated culture plate. This raises the question: What was Fleming doing for the previous two months, and if he was working with penicillin, why didn’t he bother recording any of it?

For decades, these scientific inconsistencies and experimental failures have haunted the story of penicillin’s discovery. Amidst the incontrovertible Nobel Prize-winning scientific and clinical success of penicillin — and without a plausible alternative — the doubters kept quiet. At least, most of them.

Ronald Hare’s Theory (1970)

In 1964, the bacteriologist Ronald Hare took up the puzzle of penicillin’s origins. After examining old lab notebooks and conducting experiments of his own, he would conclude that “the history of both the culture plate and the mould itself must have been very different from what had previously been thought to be the case.” Hare published his own theory on penicillin’s discovery in his 1970 book, The Birth of Penicillin, and the Disarming of Microbes.

Hare was uniquely positioned to investigate this mystery. Not only was he an accomplished bacteriologist and expert on penicillin, having spent 20 years as a Professor of Bacteriology at the University of London, and the ten years before that at the University of Toronto, where he was largely responsible for planning and building the Canadian Government’s penicillin plant; he started his career in the same department as Fleming at St. Mary’s. In fact, he claims to have been in the laboratory the very day Fleming discovered the now-famous culture plate. (Despite this close professional association, however, Hare claims to have played no part in the discovery or original research on penicillin nor to have discussed them with Fleming.)

Although that discovery is now regarded as one of the most significant scientific events of the 20^th century, Hare admits that, at the time, it made little to no impression on him or any of his colleagues. “The rest of us, being engaged in researches that seemed far more important than a contaminated culture plate, merely glanced at it, thought that it was no more than another wonder that Fleming seemed to be forever unearthing, and promptly forgot all about it.”

And yet, Hare had been skeptical from the start that penicillin could have been discovered by simple contamination of a culture plate. It was such a common occurrence in biology laboratories that “if this had been the sequence of events, penicillin would probably have been discovered while Fleming was still a child.”

After retirement, Hare took up the penicillin question. He began by attempting to replicate Fleming’s discovery. He seeded an ordinary culture plate with staphylococci, incubated it until colonies were visible, then placed a few mold spores on the surface. As the microbiologists before him had observed, the mold refused to grow. He tried coaxing the mold’s growth by plating it further and further away from any staphylococcal colonies (without deviating too far from the overall appearance of Fleming’s Figure 1).

With this approach, he was finally able to get the mold to grow and produce penicillin, but still the staphylococcal colonies were unaffected. “No one looking at such a plate could possibly guess that a powerful antibacterial substance was emanating from the mould.” If, however, he reversed the order and plated the mold before the staphylococci, he could get a result “almost indistinguishable from that of Fleming’s original plate.”

Vexed, Hare reevaluated the evidence. He had shown the mold couldn’t have contaminated the plate after the staphylococci because the mold wouldn’t grow (or, if it did, the penicillin wouldn’t affect the staphylococcus colonies). He assumed that the contamination couldn’t have occurred before the staphylococci (though that reliably recreates the plate pictured) because no bacteriologist would knowingly use a contaminated plate.

What if the mold contaminated the plate at the same time, or within a few hours, of when it was seeded with staphylococci? And what if the staphylococci’s growth had been paused (somehow) until the mold colony had matured? To Fleming’s eyes, he would have assumed he had inoculated staphylococci onto a contamination-free culture plate. Yet, with the staphylococci’s growth delayed, the mold would have had time to fully develop into a large, penicillin-producing colony. When the staphylococci’s growth was restarted, it would be growing in effectively the same conditions as if it had been plated after the mold had grown.

Hare knew just the thing that could arrest the staphylococci’s growth: low temperature. Staphylococci grow most rapidly at 98.6 °F (37 °C). As a human pathogen, it has evolved to grow optimally at human body temperature. This is why microbiologists incubate culture plates: to speed up their growth into visible colonies. The lowest temperature at which any staphylococci growth occurs, and then only very slowly, is around 53 °F (12 °C). The Penicillium mold, on the other hand, prefers to grow around 77 °F (25 °C) but is not greatly affected by temperature ranges.

It therefore seemed possible that penicillin could have been discovered as described in the original 1929 paper, but with the addition a few details Fleming was unaware of: first, the inoculation of staphylococci and contamination by mold occurred at the same time; second, Fleming forgot6 to incubate the plate; and third, the lab’s room temperature was low enough for long enough for the mold to grow and produce penicillin before the staphylococci began to grow.

To test this theory, Hare simultaneously inoculated a culture plate with both staphylococci and Fleming’s mold and left it on his benchtop. The weather that day was cold, wet, and stormy, and the temperature was relatively low: 61 to 65 °F (16.1 to 18.3 °C). As expected, the staphylococci grew more slowly than they would have in an incubator, and only tiny transparent colonies were visible on the third day. The mold, however, grew much more prolifically, and a tiny colony was visible after just 48 hours, growing to 10 mm by the fourth day.

By the end of the fifth day, Hare had rediscovered penicillin. The result was practically indistinguishable from the photo in Fleming’s original paper: in a ten millimeter zone around the mold, the staphylococcus colonies were small and transparent, while those outside the zone were larger and opaque. Many experiments later, Hare found that penicillin could reliably be rediscovered in this manner so long as the temperature was kept below 68 °F (20 °C) for four or five days.

This is where Hare the scientist had to become Hare the historian. Was the temperature in Fleming’s laboratory low enough for him to discover penicillin at the end of July or the beginning of August in accordance with the timeline of his canonical story?7

Hare searched the records at the Meteorological Office for the maximum and minimum shade temperatures from the beginning of July to the end of September, 1928. In the weeks before Fleming left on holiday there was a heatwave; from July 10^th to 27^th, there were highs in the upper 70s and 80s. At these temperatures, the staphylococci would have grown too quickly.

However, on the 28^th, the heatwave ended and was quickly replaced by a cold snap. For the next nine days, the maximum temperature only exceeded 68 °F on two occasions, and not by much. It was a slim window, in which the temperature in Fleming’s laboratory would have been low enough. But it coincided perfectly with Fleming’s holiday.

Hare’s theory relies on a triple chance of unlikely events. First, the penicillin-producing Penicillium mold landed on Fleming’s culture plate; second, Fleming failed to incubate the plate; and third, the temperature was low enough for the five days required to favor mold growth.8 “Had only one link in this chain been broken,” Hare writes. “Fleming would have missed his opportunity.”

Hare himself concedes that the combination of these contingencies seems exceptionally unlikely. The original story of chance discovery, on its own, was one of serendipity and good fortune. His theory required an additional layer of meteorological luck on top of chance contamination. “Far from the phenomenon that led to the discovery being a comparatively common event that had previously escaped detection, it must be so unusual an occurrence that it is doubtful whether it can have happened very often since bacteria were first cultivated in the laboratory.” Yet, however improbable it may seem, to quote Sherlock Holmes: “When you have eliminated all which is impossible, then whatever remains, however improbable, must be the truth.”

Robert Root-Bernstein’s Theory (1989)

Hare’s theory is based on the assumption that the Figure 1 plate was indeed the source of the original contamination. It also overlooks the two-month gap between when Fleming allegedly noticed the contaminated plate and recorded the first penicillin experiment. These details, however, form the foundation of a competing theory on penicillin’s origins — that belonging to Robert Root-Bernstein, Professor of Physiology at Michigan State University.

Root-Bernstein described his theory in his 1989 book, Discovering: Inventing and Solving Problems at the Frontiers of Science.9 It’s an ambitious and unorthodox book, structured as a seminar between six characters discussing creativity and the scientific process. Each character represents various points of view on the sciences and scientists and, along the way, they also discuss the important chronological and methodological idiosyncrasies of Fleming’s discovery.

Root-Bernstein’s theory is argued and defended by the character Imp (real name Ernest; apparently a stand-in for the author himself). After summarizing the key details of Hare’s theory, Imp focuses on the two-month gap. Fleming supposedly discovered the Fig. 1 contaminated plate when he returned from a holiday on September 3^rd, but the first lab notebook entry about Penicillium and penicillin wasn’t written until October 30^th. As described earlier, that entry does not record the discovery of a contaminated plate but a planned experiment in which the Penicillium mold was first isolated and tested against several bacteria, including staphylococci.

But why, Imp wonders, if Fleming already had that beautiful culture plate which so perfectly illustrated the staphylococci-killing power of penicillin, he would wait two months to record the finding? And why do so in the context of another experiment? Furthermore, this plate still exists within the British Museum. That means Fleming had to fix it with formaldehyde relatively soon after he found it. But if he thought the plate was important enough to preserve, why didn’t he note its discovery at the time?

It wasn’t in Fleming’s character to procrastinate. According to his research scholar, Merlyn Pryce: “[Fleming] didn’t confine himself to observing, but took action at once. Lots of people observe a phenomenon, feeling that it may be important, but they don’t get beyond being surprised — after which, they forget. That was never the case with Fleming.” So then, what was he doing for two months?

It’s in this context that Imp (Root-Bernstein) grounds his belief that Fleming’s discovery wasn’t the serendipitous chance of lore — at least, not completely. Instead, he proposes that Fleming wasn’t running a staphylococcus experiment when he discovered penicillin; he was looking for new sources of lysozyme.

Fleming had a long-standing professional interest in antibacterial substances. His most important discovery before penicillin was the lysozymes, enzymes found in various bodily fluids (e.g., tears, saliva, and egg whites) that break down the cell walls of bacteria. He had also studied the antibacterial properties of mercuric chloride and bacteriophages.

Between 1922 and 1928, Fleming’s team tested anything they could get their hands on: human mucus, tears, sputum, and blood; the eggs of dozens of fish and bird species; tears collected from horses, cows, hens, ducks, geese, and fifty other species from the London Zoo; earthworm and snail slime; large numbers of vegetables and flowers. They continued to publish on lysozymes into the 1930s. “Is it too much to suggest,” Imp asked, “that he also examined any fungus that happened to come his way?”

If we assume that Fleming was engaged in a systematic search for new sources of lysozyme, we can now reasonably fill in the gap between September 3^rd, when he first spots the mold, and October 30^th, when he first records the Penicillium experiment. Root-Bernstein’s theory about the discovery goes like this:

First, Fleming begins by finding the mold, which may or may not have been on a staphylococcus plate. In the paper, Fleming only says that he found it at the time he was “working with staphylococcus variants.” Either way, the plate is not enough to incite a “Eureka!” moment, as the canonical version of the story suggests.10 Instead, like the hundreds of other unusual samples he’s tested, Fleming transfers the mold to a new culture plate, gives it a few days to establish itself, and then runs a routine experiment to test for lysozyme activity. He finds that it weakly affects a lysozyme-sensitive strain. Not terribly interesting — not even worth recording11 — but it warrants a follow-up.

A short time later, the Root-Bernstein theory goes, Fleming prepares a second experiment. After growing the mold for five days into a robust colony, he adds various lysozyme-sensitive and -resistant species to the plate, including Staphylococcus. This time, he records the results because (surprise!) the mold affects the lysozyme-resistant staphylococci. This experiment, whose results are recorded on October 30^th, is exactly what it appears to be within the context of Fleming’s notebooks: “the first penicillin experiment — the first recognition by Fleming that he’s dealing with something unexpected and exciting!”

Yet, if this is the true sequence of events, why didn’t Fleming record it as such in his 1929 paper? “The logic of presentation rarely corresponds to the logic of discovery,” said Imp. Few scientists actually document the chronological sequence of events that led to their discovery. “Just imagine for a moment trying to write into a research paper the account I’ve just given,” said Imp:

While looking essentially randomly for organisms producing lysozyme, a common but unidentified mold was isolated from the air of the laboratory. Initial experiments showed that the mold appeared to have lysozyme activity, so controls were set up, including staphylococci, which I just happened to have been working on at the time. Much to my surprise, the mold had unexpected properties, so I was now forced to further characterize and identify the mold …This subsequent research conclusively demonstrated that the product of the mold was not lysozyme, but rather a new substance having the following characteristics …

It’s too circuitous and indirect for a scientific report. Better, instead, to start with the mold lysing the pathogen, because that was the important and novel observation.

Under this theory of events, the Figure 1 plate also becomes exactly what it appears to be in its proper context: an illustrative example of the fact that penicillin-secreting Penicillium can kill staphylococci. Not, as the story is typically told, the original contaminated plate. Reading further in the paper, similar examples are included as Figures 3 and 4, which illustrate other properties of penicillin.

Fleming still could have shown his colleagues a contaminated staphylococcus plate on September 3^rd, but one which must not have had the telltale “ring of death.” Or perhaps he did pass around the plate that would become the famous Figure 1, but not until several months later, when he was preparing figures for his paper. Hare’s cold snap, too, may have played a role in the mold growing when it did, but it no longer has to coincide with Fleming inoculating his staphylococcus plate.

That Fleming was originally searching for new sources of lysozyme could also explain why he thought the mold contaminated a staphylococcus plate after the colonies had fully grown (which, barring Hare’s theory of simultaneous contamination, should be impossible). Penicillin may not be able to lyse mature colonies, but lysozymes can. Fleming may have assumed penicillin lyses bacteria the same way as lysozymes, and therefore could lyse mature colonies. It’s a conceptual leap, but one made smaller if he was looking for lysozymes in the first place.

Like Hare, Root-Bernstein does not claim his account of Fleming’s discovery is “true,” only that it’s compatible with available data. (Root-Bernstein does not, however, shy away from claiming that his theory is the more likely of the two. “Hare may be a good bacteriologist,” said Imp, “but I question his historical acumen. Dates — you’ve got to pay attention to dates.”)

More important to Root-Bernstein than the specifics of Fleming’s discovery is the fact that it evidences Pasteur’s principle that “chance favors only the prepared mind.” Whether he was experimenting with staphylococci or lysozyme, Fleming kept his mind open to the possibility of discovering new bacteriolytic substances. He often gave the advice, “Never neglect an extraordinary appearance or happening. It may be — usually is, in fact — a false alarm that leads to nothing, but may on the other hand be the clue provided by fate to lead you to some important advance.”12

Fleming’s methods — which included testing strange samples and keeping plates around for longer than he needed them — increased the probability that he would stumble upon something new, and he was mentally prepared to recognize them when he did.

Source of the Mold

The other important aspect of Fleming’s discovery is the source of the contaminating mold. According to the canonical version of the story, the Penicillium floated into Fleming’s lab from an open window. However, no such claim was made in the 1929 paper. In fact, nothing about its source was said until 1945 when Fleming told the writer George Lacken that it had blown through the window from Praed Street.

Why Fleming would say this is a mystery. He had no evidence that was the case, and as Hare writes, opening a laboratory window is “thoroughly bad bacteriology.” Further, Fleming’s windowsill was often piled high with test tubes and beakers filled with pathogenic bacteria. It would have created quite a scandal should any of these have fallen out of an open window onto the heads of the vulnerable passersby below. Nevertheless, the story gained wide publicity after André Maurois repeated it in his 1959 biography, The Life of Sir Alexander Fleming. Maurois repeatedly referred to “the mysterious mould from Praed Street,” and “the spore carried by the wind.”

Fleming himself seemed unsure of its origins. In a 1946 speech at the Mayo Clinic, he claimed ignorance of its source, “a mould spore coming from I don’t know where, dropped on the plate.” But in another speech in Edinburgh that same year, he claimed, “penicillium had dropped through the window.”

In Hare’s account, the Penicillium came not from the window but the stairwell. In Hare’s 1970 book, he notes how immediately below Fleming’s laboratory, in the same turret of the building, was a mycology lab run by C.J. La Touche. La Touche studied how molds can trigger asthma. He spent much of his time swabbing carpets and curtains in homes inhabited by asthma patients and growing strange and uncommon species of mold from these samples. In the process, he had acquired quite a large collection. But, as Hare recalls from his time working in the same building, La Touche’s lab wasn’t equipped with the fume cupboards or hoods that most mycologists used to prevent mold spores from contaminating the air. As a result, the air in La Touche’s was liable to be full of floating spores, waiting to be carried wherever the breeze might take them.

Both La Touche and Fleming’s labs had doors that opened to a shared stairwell. It is therefore likely that the spore that contaminated Fleming’s plate had originated in La Touche’s laboratory, having traveled out the door of La Touche’s lab, up the stairs, and into Fleming’s. Yet even if none of La Touche’s spores took this journey, at the very least, La Touche himself did: Fleming cites La Touche as the mycologist who identified the mold as Penicillium.

Theories, Plausible and Implausible

As we approach the 100^th anniversary of Fleming’s discovery of penicillin, no definitive answer to this mystery has emerged. Other scientists have proposed a handful of additional theories,13 some of which rely on events even less likely than Hare’s, but Hare and Root-Bernstein’s seem to be rooted in the most solid evidence.

For what it’s worth, I believe Root-Bernstein’s theory. Hare’s is scientifically possible, but it relies on an exceptionally improbable sequence of events requiring luck on the order of picking the correct Powerball numbers three (or more) times in a row. Root-Bernstein’s is simpler and more in tune with the psychology and habits of working scientists. It only requires accepting that Fleming and his colleagues misremembered the identity of an unrecorded and, admittedly, forgettable culture plate from 15 years earlier — which seems entirely plausible. Occam’s razor suggests the simplest explanation is usually the best one, and that is Root-Bernstein’s.

The story of Fleming’s discovery of penicillin is not just an interesting historical anecdote; it’s held up as a prime example of momentous inventions discovered by accident. It looms large among discussions about the nature of discovery and how to encourage it. But if Root-Bernstein’s theory is true, and Fleming actually found penicillin while searching for new lysozymes instead of while doing an unrelated staphylococcus experiment, can it really be called an accident?

Of course, penicillin isn’t lysozyme, and a deliberate search for one thing that results in finding something else can still be deemed accidental. Yet, finding a new kind of bacteriolytic substance while looking for a different kind of bacteriolytic substance seems, at least, to be one of a lesser order. Fleming may have been fishing for lysozyme, but his methods — testing strange contaminants for the ability to lyse other microbes — formed a net that, sooner or later, was bound to catch something else.

Root-Bernstein’s theory thus turns penicillin from an example of an “accidental discovery” into one that reflects what the computational biologists Itai Yanai and Martin Lercher have described as an “evolutionary process” in scientific research. In this conception, research isn’t a linear march, but an evolutionary tree, full of once-promising branches that proved fruitless and unexpected offshoots that led to new discoveries. Such an evolutionary history, they argue, “is generally obscured in the resulting scientific publication,” which favors neat teleology.

Fleming’s 1929 penicillin paper may have been written as a linear process, but that’s almost certainly not how the discovery occurred. And by eliminating these complicated twists and turns, Fleming inadvertently obscured what may be one of the most important lessons in scientific history: how combining a meticulous research program with the openness to branch out into new directions led him to Nobel Prize-winning success. Neither rigid plans nor the winds of chance are enough on their own; discovery requires both.

Ultimately, whatever sequence of events actually occurred, what mattered was that Fleming was primed to make the key observation when chance presented it and jumped on what he saw. The rest is history.

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Kevin Blake is a scientific editor at Washington University in the Division of Laboratory and Genomic Medicine. He writes about microbiology, bioinformatics, and evolution.

Header image by Ella Watkins-Dulaney.

Cite: Blake, K. “The Penicillin Myth.” Asimov Press (2025). https://doi.org/10.62211/04kq-22ub

Further reading:

• Hare, Ronald. 1970. The Birth of Penicillin, and the Disarming of Microbes. London: Allen & Unwin.

• Root-Bernstein, Robert Scott. 1989. Discovering: Inventing and Solving Problems at the Frontiers of Scientific Knowledge. Cambridge, Mass.: Harvard University Press.

• Macfarlane, Gwyn. 1984. Alexander Fleming: The Man and the Myth. Cambridge, Mass.: Harvard University Press.

• Rosen, William. 2018. Miracle Cure: The Creation of Antibiotics and the Birth of Modern Medicine. New York, New York: Penguin Books.

Nature, mysterious in day’s clear light,
lets none remove her veil,
and what she won’t discover to your understanding
you can’t extort from her with levers and with screws.1

Goethe, Faust I, lines 672–675

Only about the size of a pinhead, the early amphibian embryo undergoes rapid cell divisions immediately after fertilization. By the time this cellular sphere comprises a few thousand cells, the embryo begins to fold inward. The point at which it does so marks the dimple-like dorsal lip of the blastopore — the opening of the embryo’s newly forming central cavity. In the early 1920s, Hilde Pröscholdt, a talented graduate student under the supervision of Hans Spemann at the Zoological Institute in Freiburg, Germany, had observed this “gastrulation” process hundreds of times under her microscope.

Spemann’s own earlier experiments identified that the dorsal lip might be necessary for the embryo’s development, but how exactly it exerted its influence was unknown. Hilde Pröscholdt developed a delicate surgical technique that allowed her to excise the dorsal lip from the developing embryo of one newt species (Triturus cristatus) with unpigmented cells and transplant it into the same-stage embryo of another newt species (Triturus taeniatus) with brown cells, opposite its native dorsal lip. Thanks to the color difference between the host and the graft tissue, Pröscholdt was able to follow their fates.

It wasn’t until after numerous attempts,2 hampered by lack of antibiotics to ward off infections and the delicate nature of the surgery itself, that Pröscholdt observed a most marvelous result. By transplanting the dorsal lip from one blastopore onto a second embryo, she was able to coax the recipient embryo to grow into a two-headed organism, a pair of conjoined twins.3

Judging from the brown coloration of the twin embryo, the transplanted dorsal lip instructed the host cells to develop a second, complete body axis. The transplant’s own cells contributed only to the second notochord (a precursor to the spine in vertebrates). Spemann thus named the dorsal lip “the organizer,” as it instructed the fate of surrounding cells, steering and organizing their development into specific organs and tissues.4

Hilde Pröscholdt (Mangold after marriage) didn’t live5 to share the Nobel Prize in Physiology and Medicine that Hans Spemann received in 1935, but the discovery of the Spemann-Mangold organizer has repeatedly been called one of the most beautiful experiments in embryology. A Cells and Development editorial celebrating the centennial of this experiment in 2024 notes:

The exquisite beauty of the skillful experiments, histological sections, and written protocols of Hilde Mangold now form part of the history of biology. Her dedication to detail and excellence in this thesis for Freiburg University is probably without parallel.

But what does it mean for an experiment to be beautiful?

While every practicing scientist has an intuitive sense of what a beautiful experiment is, these features are rarely put into words. Nor is the answer static, and like aesthetic values more generally, these features changed throughout scientific history. In the 17th and 18th centuries, aesthetic appreciation of experiments was centered on nature unveiling its innate beauty. The principal job of a natural philosopher was to “reveal” what was already there.

But in contemporary terms, beautiful experiments are those that are distinguished by the aptness of their conception and execution (that is, how fit they are for the purpose of testing a particular hypothesis), by their clarity, ingenuity, simplicity of means, and by the importance of their results. Indeed, beautiful experiments exhibit a strong information asymmetry between the input from the experimenter and the output of the system under study. In the simpler words of the theoretical physicist and Nobel Prize laureate Frank Wilczek, in a beautiful experiment, “you get out more than you put in.”6

Amazingly, these features not only make experiments aesthetically appealing but also practically valuable. They are overrepresented among the historically decisive experiments that resolved major theoretical uncertainties in biology (and in the natural sciences in general). And while it may seem that a beautiful experiment results from a stroke of genius, perhaps we can invite more elegant experiments as a regular part of scientific practice. As a first step toward learning to design beautiful experiments, we need to better understand what makes them so.

Two Modes of Aesthetic Appreciation

During the Enlightenment in 18th-century Europe, experimental science was primarily seen as a means of revealing the beauty of nature itself. There was a strong belief in nature as well-ordered and comprehensible by the human mind, and its beauty as originating in God’s design.7 The Irish-Scottish philosopher Francis Hutcheson (1694–1746) even suggested that God had arranged this mystifying correspondence between the truths of nature and our experience of aesthetic pleasure and appreciation to encourage human curiosity.

An experimenter’s job was thus to expose the underlying forces that generated a variety of readily observable effects, akin to the unifying principle of least action: patterns of sound vibrations (Chladni plates), the dizzying variety of life forms, the symmetries of snowflakes and crystals (Haüy’s “primitive forms”). If nature were a painting, the experiment was but a frame to showcase it.

Rather than being a means for testing a pre-existing theory, the experiment was the starting point of an investigation in 18th-century natural philosophy. The primacy of experiment over theory was also related to the fact that scientific inquiry was essentially inductive: knowledge was (in the spirit of the philosopher Francis Bacon) built by amassing well-made observations and demonstrations and only then distilling them into theories.8

Experiments made in this tradition focused on revealing nature’s inherent beauty while the details of experimental design remained secondary. In the 1740s, for example, Abraham Trembley, a scholar and tutor from Geneva, chanced upon a strange creature in a sample of pond water. Though he wasn’t aware of it, some decades earlier, Antoni van Leeuwenhoek had identified this creature as a “water plant,” or a polyp. But upon closer inspection, Trembley observed that it had, instead, the habits of an animal — it could move, extend and contract its body, and prey on food with its mouth tentacles.

Trembley cut the polyps in half (and in many other ways) and watched in amazement as each fragment regenerated into a whole organism. He explored variations of this captivating process and extensively documented the outcomes. Most of his experiments were conducted in the palm of his hand with a pair of scissors, sometimes aided by a weak magnifying glass. In his 1741 letter to the French naturalist Réaumur, Trembley described these budding polyps as Hydre, and Réaumur excitedly shared his findings with the French Academy of Sciences.9

Trembley himself was hesitant to theorize about the significance of his discoveries. He eventually summarized them in a 1744 treatise, Memoir on the History of Polyps. Expressions of surprise, awe, and wonder permeate his writings, alongside meticulous descriptions and illustrations. His focus — and the focus of the scientific community that enthusiastically received his findings — was on the phenomenon of regeneration itself, with the experiments merely reflecting its careful study, only later distilled into theory by Trembley’s successors.10

The late 18th and 19th centuries, however, brought about a major shift in scientific methodology. With the development of the German research university model, where teaching and research went hand in hand, laboratories became the engines of knowledge production. Scientific equipment for observation and measurement became more standardized, supporting the emerging ideal of “mechanical objectivity.” (For one, photography started replacing artistic drawings of biological samples.)

In 1840, the English polymath William Whewell articulated the changing relationship between hypotheses and experiments that had begun to dominate in this new research environment:

The hypotheses which we accept ought to explain phenomena which we have observed. But they ought to do more than this: our hypotheses ought to foretell phenomena which have not yet been observed.

This sentiment was even more forcefully expressed by the French physiologist Claude Bernard in his 1865 treatise, Introduction to the Study of Experimental Medicine:

A hypothesis is … the obligatory starting point of all experimental reasoning. Without it no investigation would be possible, and one would learn nothing: one could only pile up barren observations. To experiment without a preconceived idea is to wander aimlessly.

The experiment now served to verify and illustrate (or refute the correctness of) preconceived theories, themselves building on earlier research.11 Scientific reasoning became more deductive, following from hypothesized generalities to observed particulars.

With this shift, there was also a change in how experiments were aesthetically appreciated. The attention switched to how the experiment was designed (how fit it was for the job of testing a hypothesis), rather than on what the experiment showed (the natural phenomena themselves). The beauty on display in the experiment was now that of human ingenuity and economy of experimental operations, rather than the underlying perfection of nature.

Louis Pasteur’s refutation of the theory of “spontaneous generation” is an elegant example of 19th-century experimental design coming to the fore. Many of Pasteur’s predecessors and contemporaries were proponents of spontaneous generation of life from a nutrient-rich source (like broth or meat) in contact with air. Pasteur’s hypothesis was, in contrast, that living microorganisms can only originate from pre-existing germs carried by the air, but not from the air itself.

To test this hypothesis, he commissioned special glassware for his lab in the form of a swan-neck flask with a round bottom. He carefully poured a nutrient-rich broth into the flask, then boiled it to kill germs present in the broth, and left the flask open to the air. Owing to the geometry of the flask, the air could freely contact the broth, but dustmotes carrying germs became trapped in the flask neck’s bends. Pasteur repeatedly observed that the broth would remain clear for a long time, under a variety of conditions — different weather, altitude, or geographic location.

But when he tilted the flask so that the liquid washed the trapped dust down to the bottom of the flask, or when he snapped the neck of the flask, the broth would soon become cloudy, indicating microbial growth. The observed phenomenon itself is arguably not spectacular in this case. However, the scientific community at the time appreciated and rewarded12 the ingenious experimental design, which was able to decisively resolve a centuries-long scientific controversy.

In the words of the physicist John Tyndall, who closely followed this debate, “there is no inference of experimental science more certain than this one.” And Pasteur, for his part, harbored no false modesty about his own achievement: “Never will the doctrine of spontaneous generation recover from the mortal blow of this simple experiment.”

Beauty in Experimental Design

For contemporary scientists, as inheritors of this 19th-century outlook, the focus on experimental design itself is all too familiar. But what exactly does it mean for the design of an experiment to be beautiful?

A beautiful experiment is more than just a good experiment — one that has appropriate controls, well-calibrated equipment, and clear reasoning from data to its interpretation. Whereas a good experiment is “merely” a trustworthy one, a beautiful experiment has additional qualities on top of trustworthiness, which is taken as an epistemic baseline. Such additional qualities have been suggested by both practicing scientists and philosophers of science to include economy and aptness of experimental design, clarity, decisiveness, ingenuity, simplicity of means, and significance of results.13

To return to Wilczek’s observation that in a beautiful experiment, “you get out more than you put in,” a beautiful experiment is thus also the opposite of brute force.14 It interrogates nature by a precise perturbation of a system that produces a rich and revealing response. Making such a delicate yet compelling perturbation requires the researcher to already have a good model of the system, noticing or stipulating some patterns that can be used to compress or skip unnecessary steps. Brute force methods, in contrast, often indicate a lack of a model. Interventions based on it are crude and seize on the system’s most superficial aspects.15

We can now see why the Spemann-Mangold experiment is considered one of the most beautiful experiments in embryology and all of biology. It not only demonstrates this notion of delicate perturbation and positive asymmetry of effort but also all the additional hallmarks of a beautiful experiment. It is conceptually simple: excise a patch of cells from one embryo and graft it onto another — crucially, while being able to visually distinguish the donor and recipient tissues.

But the Spemann-Mangold experiment was also based on a strong prediction about the unique role of the grafted tissue, the dorsal lip of the blastopore. And the embryo, being the very complex and sensitive system that it is, responds to grafting by massively restructuring itself in a revealing way, confirming the organizer hypothesis. This is one of the most significant results in embryology, and it also proved to be extraordinarily generative, opening up a whole subfield of embryonic induction, still actively researched a century later.

Simplicity comes up as one of the most frequently named qualities of a beautiful experiment. It represents a consistent, “classical” aesthetic value among scientists from the 19th century onwards. This includes both conceptual simplicity, simplicity of means (equipment and procedures), and operational simplicity (few sequential steps).

Another example of such simplicity can be found in the famous polyU experiment published in 1961 by Marshall Nirenberg and Heinrich Matthaei. A few years earlier, Francis Crick postulated that RNA may be the intermediate in the information flow from DNA to proteins. The discovery of the short-lived messenger RNA had been published earlier in 1961. In a beautiful experiment, Nirenberg and Matthaei showed that a cell-free extract of E. coli could be used as a model to determine if an RNA sequence could, in principle, program protein synthesis.

To simplify their experimental setup, the duo used synthetic RNA made only of uridine nucleotides (polyU). To the cell-free extract with polyU, they added a mix of all twenty canonical amino acids, while radioactively labeling only one of them at a time. Only when phenylalanine was labeled were they able to isolate a polypeptide made entirely of that amino acid, indicating that some number of U nucleotides encodes it (the triplet nature of code wasn’t revealed until later in another set of elegant experiments by Francis Crick and colleagues).