Inside ARIA, the UK's Bet to Build Scientific Revolutions

An interview with Ilan Gur, CEO of ARIA, about the organization’s efforts to build scientific waves.

The UK’s Advanced Research and Invention Agency (ARIA) is often referred to as a “UK DARPA”. While ARIA is no DARPA clone, many features of the agency are admittedly DARPA-inspired, such as the use of term-limited program managers, which ARIA calls program directors. These program directors serve as chief visionaries for their programs as well as fund and actively manage teams of coordinated external researchers towards a program's well-defined goal. Despite these similarities, the founding team at ARIA views their work as a metascience experiment all its own. ARIA’s ultimate aim is to drive economic output, quality of life improvements, health benefits, and innovation in the UK. The strengths, needs, and context of the modern UK R&D ecosystem shape the agency’s structure at least as much as lessons from DARPA history. 

Any given ARIA program is meant to catalyze progress towards big-if-true, non-consensus ideas. These programs each represent different bets that fall within what ARIA calls ‘opportunity spaces.’ Opportunity spaces delineate areas that ARIA and its program managers believe might be ideal places to create big-if-true technology waves.The expectation is not that each program achieves positive results, but instead materially “changes the conversation” regarding what’s possible in a space. 

To better understand the ARIA experiment, Eric Gilliam, author of the FreakTakes blog and expert on the history of R&D organizations, sat down for a three-hour interview with Ilan Gur, CEO of ARIA. Prior to joining ARIA as its first CEO, Ilan was a founding program manager at ARPA-E, the founder of a lithium battery startup, founding director of Cyclotron Road, and founder of Activate. At ARPA-E, Ilan took a special interest in finding better ways to commercialize exciting research. At Activate and Cyclotron Road, he built fellowships that served as perches for researchers working on societally important ‘ hard’ technologies that might not yet be VC-fundable find their feet and begin developing technologies into market-ready products.

This interview was edited for brevity and clarity, but the full transcript and video can be found at FreakTakes.

Eric Gilliam: ARIA is called a “UK DARPA,” but it’s different in many ways. How is ARIA similar to DARPA, and how is it different?

Ilan Gur: When ARIA was created, the tagline was, “A DARPA for the UK.” But we were not set up to be a DARPA. DARPA was created in the United States 70 years ago. How that model translates to the UK is not obvious. However, if you want an existence proof of a funding agency doing things differently and having massively transformative outcomes, DARPA is that existence proof.

In setting up ARIA, the U.K. government also went through a very deliberate process to make sure that it had independence and freedoms to be able to do all of the best things that early DARPA was able to do. And I think it's worth calling out that Parliament, civil servants, and others involved in this got this right. There’s not a ton of political intervention. The processes that do exist are reasonable and make sure we’re responsible stewards of taxpayer funds. But they also weren't prescriptive in what ARIA looks like. We have the freedom to build the agency from first principles. 

I sometimes say that the UK government set up a “stem cell of an R&D funding agency,” and now we're trying to differentiate it towards something that changes the world.

Fundamentally, we're meant to take bold bets that amplify different parts of the research system in new ways. I think about our programs as funding a constellation of teams that can lead to massively transformative outcomes at the intersection of quality of life and economic growth — not just for the UK, but for the world. That “for the world” bit is really about the scale of ambition that we are talking about.

E: How are ARIA’s ambitions different from, say, a deep tech venture capital firm’s?

I: While some VCs are just in it to make money, a lot of VCs see venture capital as a platform to change the trajectory of the future in positive ways. We share that vision. But the big difference between ARIA and VC is twofold. When thinking about the bar of “big-if-true,” it's important to think about both the sense of scale — “how big is ‘big’?” — and how speculative you are willing to get on the “if-true?”

In talking to VC friends about what we do at ARIA, you‘ll sometimes hear this metaphor describing startups and VCs as “surfing a wave.” A VC — the surfer — looks out at the wave set that’s coming and asks themselves, “Is that wave forming? Is it going to be a really big one?” The size of the wave is something like, “How big of a market do we think might emerge?” And the bet they’re trying to make is, “Oh, I bet that’s a big enough wave.” And they’re trying to bet on the timing. “Okay, this is when I should grab a surfboard and start paddling.” You can think of the surfboards as the companies they’re investing in.

VCs are more reactive to the system than what we intend for ARIA. VCs are often trying to find the trends they can hop on and surf that allow them to maximize the ROI of their investment in a very direct way. A venture capitalist can only fund a thesis once there’s enough momentum. I see ARIA’s job as inputting the energy to create the wave.

If you look at the spaces that we’ve carved out at ARIA, we’ve said, “Right now, everyone looks out and just sees flat water, but we believe that by pushing a little bit here or there, we can start to build a wave.” And if we can catalyze the formation of a wave that’s big enough in one of these spaces, then that’s going to catalyze all the VCs to want to jump on that wave and invest in companies.

E: When it comes to ARIA programs starting waves, how big is big enough?

I: When new program directors join our team, we give them some articles to read ahead of time, including interviews with Bob Taylor or stories from DARPA history. The main goal is to help them understand what a win looks like. For a lot of organizations and agencies, if the research you fund leads to a new product that makes an impact, that's a big win. But often, that would be a loss for ARIA.

We want to catalyze something bigger than a product, and bigger than a company. It should be more like a movement, an entirely new technology platform that didn't exist, or an entirely new industry that didn't exist.

E: I’m sure there are some waves where a funder puts in a lot of money, say, and there are already lots of researchers ready to work on the problem. But in other situations, perhaps the wave is really small and more legwork is necessary to build momentum because nobody is yet working on those problems. So how do you approach those two different types of areas?

I: There’s so much I could talk about here, so let me give an example instead. We have a program at ARIA that is run by Angie Burnett. Angie’s a plant physiologist by background, has worked in academia, worked for a national lab, and worked for the UN for a little bit. She came into ARIA initially thinking about food security. Fast forward, and she launched an opportunity space called “Programmable Plants.”

Beyond merely being underexplored and underfunded relative to its impact, there’s usually some insight that gets us excited to pursue a space. Angie’s was that when you look at some of the biggest problems and opportunities we have in the world, and think about them from first principles, agriculture is a way to address many of them. Problems like food security and climate change are massive; you need to talk in terms of gigatons of CO₂ or carbon. Angie’s view is that you can think of plants as a technology platform capable of operating at the gigatons of carbon scale.

A plant is a piece of hardware with certain functionality. In many plants, such as a cob of corn, we have engineered the functionality of that plant over many years. We have distribution channels and the ability to deliver these things at a massive global scale. The problem is that it's currently a terrible technology platform, and we're very limited in what functionality we can build in. Instead of 18 months for a new iPhone, it might take 18 years to get a viable new crop.

If you talk to most investors, they say things like, “Given the incumbents and market structure, agriculture is basically the hardest and most entrenched space to innovate in.” It's not a great place to invest given the capital, entrenched interests, regulations, etc.

Well, we see this as an exciting area to try and create a wave. Given progress in synthetic biology and forcing functions we believe are coming that will require changes in how we do agriculture, there’s a strong argument to be made that sometime in the next few decades, there will be a shift in how we approach global agriculture. You can think of it as taking the form of an ASML-type company that completely disrupts the big five agriculture companies and does things radically differently.

In the UK and elsewhere, we have amazing progress happening in areas like de novo genome synthesis. But when Angie talked to top synthetic biology researchers and told them she was thinking about doing a plant program, the reactions were, “Why? There’s so much to be done in mammalian systems. Plants are hard. They have multiple copies of the genome. It’s impossible to figure out how to transform them. It’s XYZ.”

Angie didn’t get discouraged by that. And in the early stages, she held a workshop to bring together top people in both synthetic biology and agriculture. There were probably 50 people at the workshop. One of the questions asked was, “How many other people in the room did you know when you walked in?” And I think most people knew like five out of the 50. It seemed like none of the synthetic biology people had talked to any of the plant people.

Now, I know of at least two specific cases where, when Angie started, the researchers thought working in plants was a waste of time, but have now built meaningful collaborations working on plants.

E: How did you go about creating a system in which you’re comfortable extending the programme directors long leashes to go after visions that will often not pan out?

I: An ARIA  board member recently asked me, “Isn’t one of our biggest risks right now that we created or funded the wrong programs?” And I said, “No, I don’t think that’s a risk at all.” In part because we decided to create these opportunity spaces. 

The whole idea behind an opportunity space for us is to take speculative bets. What that means is we can’t know upfront whether this is going to lead to impact. We can’t engineer that. The only way we get it wrong is if we take a speculative bet in an unproductive direction. So the point of an opportunity space is to say, “Let’s define what we think is a productive direction.” 

And an opportunity space is going to have certain beliefs that bound it. And the point is, if you can get yourself to believe these things...e.g., “Pressure on food security and climate is going to force us to do some things differently in agriculture,” “Synthetic biology is moving…” Etc... you have to imagine there is the potential for enormous value — economic and social impact — that can happen in this space. And now that we’ve bound that space and set that opportunity space, now we can make bets in that area without having to worry about, like, “Is synthetic plants the right program?” I’m not worried about it at all because we’re making a bet in a direction that’s productive. 

The only thing we now have to worry about is that we don’t do what we were made to do. What makes ARIA unique — and what’s meant to make a place like DARPA unique, certainly in the early days — is that you make a bet, then you learn something, and you can pivot and say, “Oh! Actually it’s this 5 percent of what we’ve done so far that is starting to feel really valuable. Let’s minimize the rest and 10X that 5 percent.” That’s the thing that I think will be one of the big muscles we have to create for ARIA in this next phase.

E: When is high variance between expert opinions exciting? 

I: You mean when people say, “Oh, that's a horrible idea,” how do you know when it is actually a horrible idea? Hmm.

An interesting thing someone from DARPA once shared with me was that DARPA is a mechanism to increase variance in the system. It’s something I think a lot about for ARIA, and more than anything else, ARIA was created to do things differently. 

But if you want to do things differently, you need people who see things differently. It’s one of the reasons the program director model is very helpful. But secondly, you have to break out of the strong tendency surrounding how governments currently fund research. Governments are pretty good at funding well-known disciplines and obvious problems or opportunities. This leads us to do well allocating money to solving obvious next steps in synthetic biology, or building up semiconductor R&D capacity, because of its obvious geopolitical importance.

You need to find some way to cut and slice through those tendencies. The program director model addresses questions like, “What’s a new, actionable thesis for something that’s not within a single discipline? Or maybe it is, but it cuts across technology readiness levels (TRLs).”

We hope to fund a varied set of people with a different set of incentives than would otherwise get funded. If everyone thought it was a good idea, we would introduce no variance into the system. If no one thought it was a good idea, it probably just isn’t a good idea. But if you get spiky reactions to anything you’re doing, meaning some minority thinks it can work out and sees a lot of potential, that can be exciting. In a consensus panel, that minority voice would not win out. Those are the programs that might not ever happen otherwise.

E: Can you talk a bit about how your career up to this point, in academia and ARPA-E and elsewhere, shaped your vision for ARIA?

I: A lot of my thinking on the limits of venture capital, for example, came from my experience founding a startup focused on creating a new class of high-energy rechargeable lithium-ion batteries. I walked away convinced that venture capital was too narrow an impact model for doing early-stage science, especially for industrial markets. One of the reasons I found the chance to join ARPA-E so compelling was that it was a different mode. I thought, “Wow. We get to be the biggest Skunk Works innovation funder for anything climate-related in the U.S.!”

And I learned a major lesson through my time at ARPA-E. We had access to a lot of funding, so we had the driving force. We had access to the most brilliant ideas, so we could pick and choose from the best ideas. The thing I realized was that, actually, none of that mattered. What mattered were people, institutions, and incentives. You can have all the money you want and you can have all the ideas you want,  but if you don't have the right people in the right institutional environments with the right incentives to drive progress, you're pushing on a rope.

I left my startup feeling like I had somehow been misled on the idea that “Venture Capital-backed startups are the way to change the world.” Going into ARPA-E, I wanted to figure out alternative institutional modes. What I found in the end was that, of all the environments in which I was funding research, the ones that felt most resonant and productive were either startups or the folks within academic labs that were already operating as if they were spinning out a company.

If we don’t worry about the funding model for a second and just consider, “What is a startup?” A startup is a vehicle for getting the right people into the right environment with the right incentives, completely aligned with some research mission. For everyone in an early-stage startup, the goal is to create concrete value. You get people from different backgrounds, in interdisciplinary ways, to pursue some technical goal.

The question then becomes, “How can we fund them as R&D centers?” Venture capital is not a great way to do that. Some VCs actually do fund very applied R&D and take speculative bets, and those are companies that tend to change the world. But relative to the ~$70 billion of U.S. funding to applied and basic research, you don’t have anywhere near that going into super science-y startups.

One of the things we’re doing at ARIA, then, is to ask, “How do we try and fund not just the best people and ideas, but with resonance in terms of the environments and incentives in which they work?” We are very comfortable with the idea that, using ARIA funding, a researcher might go start a company. They might also decide to leave their academic lab and just do the research as an independent researcher.

E: Can you talk a bit about the process involved in bidding for ARIA funds? It doesn’t seem overly onerous at all.

I: As an example, let’s talk about ARIA’s seed awards. For an opportunity space, a program director creates their own program informed by their own thesis. That’s where a lot of the energy and funding will go. But we also say, “We’re not the only smart people, and it’s all about increasing variance. So, let’s find other smart people and seed their ideas, which could lead to massive breakthroughs.”

For these seeds, we say, “Give us a three-page application. Tell us why you’re obsessed with this idea. And why no one else will fund it. We’ll give you up to £500k. If you win the funds, just start running at it. Hopefully, you come back with something compelling. If you do, we can double down with you. We can either make it a bigger project or even have it inspire a whole program. We will tell you within three weeks whether you got the funding.”

E: Jenny, the program director on the robotic dexterity program, said something in one of her interviews like, “I was almost disappointed that I didn’t get the chance to fund some random person in their garage.” Can you talk about your flexibility in terms of who is practically eligible to win ARIA funds?

I: All we want to do is fund the best people in the best environments. We don’t care if you’re at a university or not.

And something interesting has already come out of our openness to alternative arrangements. Early on, we had a few people who were very happy to win the seed, but told us they didn’t want to do it in their university labs. One person wanted to rent some space and do it as an independent researcher, for example. The program director talked through it with them and thought it made a lot of sense. They’d do a lot better, and they’d be more motivated.

Once we saw a few of those, we took note and tried something. The next time we did a seed call, as part of the questions, we said, “What’s the institution you’re in now? If we award you the seed, where would you like to do the work? It doesn’t have to be the same place.” The options were things like “My current university,” “another university,” “a company,” etc. And then we included “Still Undecided” as an option.

We might be the only government funding agency in the world that gives that option. I think we had ~23 percent of applicants in the next seed call say “Still Undecided.” That’s a big deal. Consider the situation: “Eric, this is a big project; it might be the most important thing you do in your life. What is the best environment for you to do this work?” And 23 percent of people decided that maybe this was their time to do a startup, or move to the UK to pursue this work at a UK university. 

E: I’m a big Warren Weaver fan. He was maybe the greatest scientific grant funder of all time. He had the conviction that there was a “wave not yet gathering its strength” in the area between biology and physics. He put 80 percent of his yearly budget, starting in 1933, in that underdeveloped area. Five years later, he gave the field the name it now goes by: molecular biology. My question is: if ARIA felt it had an ARPAnet or a molecular biology on its hands, how much is too much of your funds focused on that one area? There’s maybe a limit. 80 percent is a lot, for example.

I: Before recruiting more program directors, we looked at our budget and current program directors and decided that we weren’t quite touching enough surface area. There were still some very exciting opportunity spaces left untouched. But we’ve also said, “There’s a limit.”

ARIA will recruit a set of program directors every other year. Given their three-to-five-year terms, that means a steady state of 15-20 program directors. That’ll be it. Our early opportunity spaces might touch a lot of surface area. But what success needs to look like is that, out of these spaces, we find something that we not just want to double down on, but 10X on. If a big portion of ARIA’s budget does not end up in one of those areas over the others, there’s a problem.

That’s my take, at least! I’m on a term limit, too! I probably won’t be the CEO when they have to figure this out. But is that 80 percent? I could imagine it.

If the ARIA CEO were convinced, they could make that call. Our governance permits that kind of decision-making. The question is: will the organization have a culture that leans towards the bold bet?

And we should be bold even in areas where VCs and other transition partners might not see the vision from day one. Some ARPA agencies, for example, require cost share in their projects. They want proof that someone else has skin in the game, so they ask some group to fund 20 percent of the project. We’re not going to do that. That could just as easily be a counter-indicator for us.

We hope to leverage other funders as follow-on partners as much as possible. But we want to make sure there’s nothing that prevents us from doing the bold thing. We might sometimes have to be the follow-on funders to some of our early-stage bets. But if the program is ambitious and we believe in it, I hope we build into the agency a culture where leaders are celebrated for doing the bold thing.

E: Do you consciously think about the idea that you have to be or find the next Warren Weaver or JCR Licklider? Does that keep you up at night?

I: What keeps me and our team up at night is actually having a massive enough impact. Do we think about trying to be or find the next Weaver or Licklider? Probably not. I use an analogy often of being a catalyst or an enzyme. Whether it's me or our team, we're something you introduce into the system that hopefully mobilizes a bunch of other factors to make an impact.

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Eric Gilliam researches 20th-century R&D orgs with the goal of improving the modern R&D ecosystem. He writes operational histories of R&D on his FreakTakes substack. He is an Associate at Renaissance Philanthropy and Fellow at the Good Science Project. At Renaissance Philanthropy, he is working to help build more ‘BBNs,’ R&D organizations inspired by early ARPA’s best contractors.

Cite: Gilliam, E. “Inside ARIA, the UK's Bet to Build Scientific Revolutions.” Asimov Press (2025). DOI: https://doi.org/10.62211/56ue-23jk