The Orthogonal Bet: How deep science ventures redefines deep tech innovation

Samuel Arbesman:

Hello, and welcome to The Orthogonal Bet. I'm your host, Samuel Arbesman. In this episode, I speak with Dominic Falcao. Dom is a founding director of Deep Science Ventures, which he created in 2016 after leaving Imperial College London Science Startup Program. Deep Science Ventures takes a principled and problem-based approach to founding new deep-tech startups. They have even created a Ph.D. program for scientists specifically geared towards helping them create new companies.

I wanted to speak with Dom to discuss the origins of Deep Science Ventures, as well as how to think about scientific and technological progress more broadly and even how to think about new research organizations. Dom and I had a chance to discuss tech trees and the combinatorial nature of scientific and technological innovation, non-traditional research organizations, Europe, and the tech innovation ecosystem there, what scientific amphibians are, and even the use of AI in the realm of deep tech. Let's jump in. Dom, great to be chatting with you, and welcome to The Orthogonal bet. I'd love it if we could start by maybe you exploring, explaining a little bit, the nature and origins of Deep Science Ventures. What are the ideas underlying what led you to create this?

Dominic Falcao:

Thank you so much for having me on the podcast. So, Deep Science Ventures, I guess, the name is actually a bit of a misnomer because I'd say that the science we do isn't deeper than the average science. We're not discovering things. We're more combining things we understand, but we do create ventures. So, a better name would probably be Combinatorial Invention Ventures, but it's got more syllables and it's harder to say.

Samuel Arbesman:

That works.

Dominic Falcao:

So, my co-founder and I used to work at Imperial College's Tech Transfer Office. And Imperial, one of the most innovative universities in the world. It costs roughly $50 million in research funding to create a spin-out at Imperial College. And the question that we looked at carefully when we were sitting in the spin-out team at Imperial was could you do this much, much more efficiently?

Are there ways of getting to that end output of a high-impact, high-growth science company, one that brings impact into the world that don't require a tortuous two-year negotiations with the tech transfer office, the five years in the desert of trying to work out what the application is, and then finally hitting on a commercial application that makes sense before realizing that, actually, there's a better technology all along in someone else's lab?

The way that we then took that process was to ask what if we didn't start at all with the technology? What if we started instead with the outcome we're trying to achieve in society, and then we treat the process of building a deep-tech company as a search question, and then we think about ways we can make that search as efficient as possible?

Samuel Arbesman:

I imagine you might be working with tech transfer offices in some university setting, but it's much more first principles, like trying to say, "Okay. What are the needs and the gaps and how to work backwards and figure out what are the components that need to get to the solutions that you're thinking about?" Is that the right way to think about it?

Dominic Falcao:

That's a really good way of thinking about it. The main difference between DSV and other studios that work in deep tech is that we do a lot of the invention in-house. So, what you'll often find is that even if a studio does its ideation in-house, they'll then still go and license the intellectual property from a university. Very rarely is that the case for us. We're normally building the entire scientific concept internally. So, we've got a team of 30 techno-commercial inventors in different specific sub-disciplines.

We've focused on four different sectors, therapeutics, agriculture, climate, and computing. And those teams are focused on starting with societal outcomes, combining things that we understand from across different disciplines into novel concepts. So, it's more like invention and less like discovery. And it's more like invention and less like translation.

I don't very often have to have long and difficult conversations with tech transfer executives, which is an absolute pleasure, but we do get to still take things that are big movements in what we understand and translate them. It just may be that they won't be from a single university or from a particular geography with trying to find the best piece of knowledge for the given requirement we're trying to fulfill for the specific product we're trying build for the particular societal outcome we're trying to achieve.

Samuel Arbesman:

And so, then in terms of the societal outcomes, how do you figure out what those are, which are the ones you want to prioritize, and how do you, I guess, work backwards? Because I imagine there's an interesting situation here in terms of a lot of scientific research and technological innovation is fairly undirected, but in this case, you're trying to figure out, at least for a subset of it, actually using a certain amount of directiveness, goal directiveness, as a way of doing this kind of thing much more efficiently. So, how do you balance those? How do you choose the problems and the outcomes you want?

Dominic Falcao:

And that's why the word science in our name is a bit of a misnomer. Whilst we're typically drawing things from fields that people recognize as science, chemistry, biology, artificial intelligence, material science, aeronautics, et cetera, we're not actually doing discovery research. So, we're not going in and characterizing something. Instead, what we're doing is we're starting with a... each team has a specific societal outcome that they're trying to achieve.

So, in our climate team, for example, it's trying to reduce the peak heating that the world goes through. Then what they'll do is put together a set of requirements for what has to be true. And that set of requirements will be underdetermined. So, there'll be different possible routes to hit that outcome. And so, I've heard you talk a little bit about technology trees in the past, Sam. The question that we ask is how can you have an immortal technology tree, something that doesn't change as the technology landscape changes?

So, your technology tree is out of date immediately, but we want to have pathways to achieve these outcomes that are not immediately out of date. So, how do you do that? If you make your tree or graph in terms of requirements instead of in terms of technologies, then it can be immortal in some sense. So, you could say this pathway, say, it's removing carbon from the atmosphere, we know that if we want to use all of the sunlight that hits the Earth's surface, we have an energy boundary. That direct air capture technology has to fall below-

Samuel Arbesman:

Right.

Dominic Falcao:

... if we want to be successful in using this pathway. And you don't need to specify direct air capture for that to be the case. It's true for any technology which is going to remove carbon from the atmosphere. It represents a kind of energy limit for us. And so, we take those pathways. We look at competing strategies. And at any given moment, we can evaluate those pathways for possibility. We can say, "Okay. At this precise moment in time, given the technologies, we can identify this pathway is possible or it's not possible."

And that allows us to prioritize what we focus on. In some cases, something not being possible is a very good reason to focus on it. It represents a barrier to entry in terms of how people perceive that pathway. If you, yourself, can see ways further down the train, down the requirements graph, that you might flip those outcomes to be possible, you might then flip the entire pathway to be possible or you may decide it's not possible for reasons that are not amenable to invention today and actually require further discovery work and further science. In those cases, we would triage those opportunities into a different bucket.

We'd maybe send those to a research agency or a philanthropy who's interested. And we'd say, "We think it would make a critical difference to conduct research this pathway." And in some cases, we can see that it would be possible, but it wouldn't be commercially tractable because the economic feasibility just isn't there. In which case, we may triage it into a different bucket again. Instead of being a high-impact, high-growth science company, it's now going to be a high-impact non-profit. So, we've done each of these things lots of times in the past. And the main visible outcome of that for us is ventures, which is where the name comes from.

Samuel Arbesman:

Got it. Okay. Well, this is really interesting. You've talked also a little bit about, and I'd love to hear more about this, of when it comes to science commercialization and discovery, the relationship between novelty and uncertainty, DSV, I think, has a fairly unique role in how to think about that. I'd love to hear a little bit more about how you think about the balance between those different things.

Dominic Falcao:

When I say that we are applying an engineering mindset to science, we are talking about uncertainty that is amenable to having engineering hypotheses leveled data. I would rather have uncertainty of the kind that, component A, which I understand very well, combined with component B, of a kind that I understand very well, will achieve outcome C, rather than I don't really understand outcome A. It's a new thing-

Samuel Arbesman:

Okay.

Dominic Falcao:

... that we've now recently characterized, combined with outcome B, which we know is true. That, within component uncertainty, is something we try to minimize, but the between component uncertainty is something we're open to because technology very rarely fail for the reason of combining known outcomes. They typically fail because there was something about a sub-technology that we didn't understand well enough, which is more common for more recent discoveries and less common for less recent.

Samuel Arbesman:

There's a phrase that, I guess, someone in Nintendo used to talk about in terms of how they made some of their innovations. I think it was lateral thinking with weathered technology or lateral thinking with withered technology. I don't know if you're familiar with this, but the idea behind it is rather than using the most cutting-edge technologies to make advances, in this case, gaming and things like that, combining pre-existing really well-known and well-studied technologies that are maybe not even close to the cutting edge, but they've been around for a while, but if you can take these things off the shelf that are really well understood, you can combine them in novel ways, which is the idea behind the Game Boy.

The Game Boy didn't necessarily have any specific new technology. They were able to just take these things that were really well understood and relatively cheap, combine them in an interesting and novel way, resulting in the Nintendo Game Boy, which has then did very, very well.

And is that the way you're thinking about that of saying, "Okay. There's a lot of really cool new technologies and new scientific advances. Those things are great, but they have not yet proved themselves yet. And so, therefore, we want to look to the shelf of things that are much more well understood. We can figure out the bounds of them and then combine them in novel combinations, two yield ways of helping get the outcomes we want."? Is that the approach that you take?

Dominic Falcao:

Yes, exactly. It's not that we discovered the iPhone or we discovered the Tesla Roadster, right? When I say, "We," it wasn't me. Elon combined the carbon fiber reinforced polymer body with flat-pack batteries and front and rear engines and removed the transmission. And together, you've got something novelty that breaks a boundary and achieves a economic outcome that wasn't possible before those things were combined, but there were no actual novel components there.

The reinforced polymer body was something that the Airbus 350 already had. It was translating technology from one industry into another that made that possible. One of the things that we observed in starting DSV is that a challenge in doing this is that this disciplinary specialization constrains solutions to a specific field when we need them from multiple fields and being able to traverse multiple fields and multiple sectors in order to get these combinations efficiently. So, to conduct that search efficiently requires a different kind of innovator, pushed to think in a different kind of way.

Not, "I've got a technology. How can I apply it?" Instead, a very difficult question, which may require knowledge from various different domains in combination, "How do I appraise those in combination to understand the possibility of them solving that particular problem?" That represents a form of uncertainty, but it's a more tractable form of uncertainty that more resembles engineering than discovery.

Samuel Arbesman:

And so, what is the ideal look or background of a person who is good at that kind of thing? Is it someone who is very comfortable overcoming jargon barriers, they know a little bit about many, many different domains, they are comfortable with a certain amount of uncertainty? But what is the profile of someone who is good at the kind of thing that DSV does?

Dominic Falcao:

I sometimes call them amphibians, but then people picture the whole of DSV as axolotls or something. So, there's a really famous quote from Stewart Brand, writing about the founder of the MIT Media Lab, where he describes him as an amphibian, comfortable both in the world of business and in the world of academia. And I think it's very apt. The ideal kind of inventor at DSV is techno commercial. They're neither purely technical nor purely commercial. They see not technical constraints. They see techno-commercial constraints.

They see only constraints that have a bearing on the commerciality of their product or technology. And so, I very firmly reject the broad idea of scientists can't be founders or the scientists shouldn't be a CEO because I find it easier for a CEO to become fluent in the language of commerce than the other way around and to understand the bearing of changing one technical parameter on the commercial model than the other way around.

So, it's typically these first principles thinkers who can understand the core assumptions and question those assumptions, who are willing to consider things that immediately appear impossible and understand, at the next layer down, why those current things are impossible and what constraints might be flipped in order to make them possible, who are willing to lean into that flipping, so to say things that are the opposite of the received wisdom until they're sure that it's untrue.

They're typically very good at extracting and understanding knowledge or they are very willing to have conversations in fields that they know nothing about. We do some training on cognitive task analysis, which is how you rapidly acquire expertise in a field to try and tune that up. In some of our founders, for example, they are ideally very persuasive. They understand or can quickly empathize with the prize that you may have, and they can tune a narrative to it. My head of talent's going to kill me for getting this wrong, but it's something like 48 different characteristics that we appraise in an individual when we're bringing them on to DSV.

Samuel Arbesman:

Oh, wow. Okay. That's pretty impressive. That also reminds me a little bit of, I mean, less about the 48 characteristics, but also just in terms of the amphibians and people who are somewhat outliers but comfortable in the world of business and technology are not quite fitting in any specific thing. The positive way of saying is that they are equally comfortable in all of these. You could also say, the more realistic, is they don't quite fit in all these different things.

And one of the things that I think a lot about is both outlier individuals within organizations as well as organizations themselves that are more willing to do either outlier activities or intermediate more interdisciplinary work or work that doesn't necessarily fit in a university or fit within just the business world. I feel like DSV is an example of some of this kind of thing. How do you think more broadly about the space of institutions that allow people to either spin out companies or create new types of research?

One of the things I were chatting before the recording around, there's obviously a lot of activities that are very valuable for science, but only a small subset of those things are the things that get you tenure. And we need more places for people to do those other kinds of activities. And I feel like DSV is one of them. Do you see a future for more types of institutions? Is this, in the long term, DSV will be a place where many, many of those kinds of people can do these kinds of things? Is it something we need a whole constellation of organizations? How do you think about that?

Dominic Falcao:

I would love for that to be the case. And I hope that we can bring on more and more people who don't fit the standard mold of existing institutions. I think about institutional diversity as being a prerequisite of idea diversity. And in particular, I think about institutional diversity with respect to outliers as the diversity of their filter. So, if we always use the same filtering conditions for thinkers in accepting them to institutions, then we'll always get the same kinds of ideas, and we won't see progress.

And one of the hard problems in improving the receptivity of an institution to an unusual person is that, in many cases, the reasons why we have those criteria in place is that they make sense, right? It's the same when you are reviewing a research paper. I was just reading this book, Everything Is Predictable. And the author makes the point that, say, you have two research papers in front of you, one by Einstein and one by me. Your priors are accurately going to tell you that you should pay more attention to the paper by Einstein than by me, a person who's got absolutely no background in quantum physics.

And so, the challenge of overcoming the selectivity of science in including radical and outlier thinkers is that it's rational to have those priors. It simply is the case that it's probably more likely that Einstein is going to have a more interesting idea than I do in quantum physics. And in this particular instance, it's correct, right? It's the same with almost every other thing that we use as a filter, whether or not it's the credentials that they have or the legibility of the idea or the legibility of the way they communicate or whether or not the idea is constrained.

One of the reasons why Kariko was in the desert for so long was because that idea was constrained. There was a number of reasons why it didn't make sense to have mRNA vaccines. They were unstable. They caused inflammatory responses. There was no immediate and obvious application as a therapeutic. That was neglected pathway. And these are all very good reasons. The challenge is that, without institutional diversity and without diversity of the set of filters on those institutions, there was no opportunity.

There needs to be one in 10 opportunity for someone like that. They knock on 10 doors, and one of them has a filter which allows for an idea to be illegible or for a person to have an unusual background. And so, that's one of the things I'm particularly passionate about in a European context is I don't think we create enough new institutions, especially scientific institutions, receiving unusual backgrounds and profiles and varying the conditions under which we accept outliers.

Samuel Arbesman:

Related to the European mode, and I want to go back to some of the other stuff, but you mentioned Europe. Do you think one of the reasons there hasn't been many institutional innovation is just because there's so many older institutions? I wonder is it one of these path-dependent things of Europe has very old universities in a way that the United States, for example, does not, and so therefore, I mean, if you start something in the United States, you're not competing against something that's 1,000 years old, you're competing against something maybe, best-case scenario, is a couple hundred years old, which is still old but not as old? Is there something there in terms of just like there's more willingness to experiment because you're not really competing against things that are as old or are there other reasons you think?

Dominic Falcao:

That's a really good observation. I've been in a situation where I've made a case for alternative institutions. And I've been construed as criticizing our existing institutions. And there is an implicit criticism. I mean, if I say we need new types of institutions, people say, "What's wrong with Oxford? What's wrong with Cambridge? These are fantastic institutions."

I can say, "Well, you can agree with that and still say that it would be good to have additional types of institutions." We are very proud of them. The other kind of problem that we have is that our more recent institutions, in the UK at least, have not been more successful than our older institutions. And so, people see a trend there. They say, "We've tried new things. We created lots of universities in the 1950s. And they're not better than the universities we created in the 1300s. So, why should we create more?"

Then again, we have institutes, research institutes, that have been very effective and have been created more recently. And so, there seems to be a willingness to create new research institutes in Europe. We've got something like 40% of the world's best research institutes in Europe. And not all of them are 1,000 years old. Some of them are more recent. So we have been able to supersede in that way, but the challenge is that, for me at least, that that comes quite late as an intervention, and they're almost always attached to existing universities.

At least in the UK, new research institutes tend to be collaborations amongst universities. In order to even get the title of research institute, you need to have a certain number of academics who've published a certain number of papers. And so, you need to get them from somewhere else. More difficult is in order to be funded, you have to have certain status in the UK. And so, there's actually a number of different... There's perception barriers, there's regulatory barriers, and there's also oligarchic research institutional reasons why it's hard.

Samuel Arbesman:

I think the interesting... the other point when you're saying of, at least in the UK, new universities have been made, they haven't been able to compete necessarily quite as well as the ones that are closer to 1,000 years old, and so therefore, what is the point, I think the argument is, and exactly what you're saying, which is these are not necessarily trying to do the exact same thing as these other universities.

Universities are great, but there are many other activities for science that are very valuable, and we need to create new institutions that allow for people who can actually thrive doing those activities to actually succeed. The question then becomes, exactly what you're saying, if they're still connected to universities, then even if, on the surface, they seem fairly different, on the one hand, they might not be as different, but also even if the people who are trying to do interesting new things go to those institutions because they're still playing in the academic adjacent world, they're probably still thinking in the back of their mind, "Oh, if this doesn't work out or I want to do something else, I probably need to make myself look legible to the world of universities."

And so, therefore, they still end up playing the traditional tenure track game, which means they can't do the really different things. And ideally, the end state might be like entirely alternate ecosystem, like parallel ecosystem, where people can bounce around doing lots of different things. That would be great. How would you get to that, though?

Dominic Falcao:

I've been building DSV for eight years. It's the question that I have in my mind. There's obviously incumbency capture in the game of creating universities and research institutes. You're right that in order to start a new one, you have to have a Nobel laureate or an existing really well-established academic at the helm in order to have any credibility whatsoever. And so, the ability to drag yourself into a differentiated space is very much constrained by that factor. The alternative option is to have a billionaire who believes in the vision behind you.

And the problem with Europe is that we don't have so many billionaires wading into the research game as the U.S. has. You've got Arcadia, and you've got the Arc Institute in the U.S. We don't have so many of those in Europe. You have Xavier Niel who created an undergraduate university school, 42, for computer science. You have less on the scientific ecosystem, which actually, I think, is a really good opportunity for any American billionaire who are listening to the broadcast because it means there's a lot of dry powder in Europe in terms of very interesting, weird, differentiated thinkers in Europe who don't have a home.

Samuel Arbesman:

Do you think, long-term, in the absence of those institutions, a lot of the talent that is in Europe will end up just moving to the United States in order to have that opportunity to fit into these organizations, or there will always be talent wherever and just it's a matter of finding people who are able to bankroll these large new types of organizations?

Dominic Falcao:

I want to say no because I want people to stay in Europe, but it's inevitably yes, you can get funding for your research and you can find someone who's willing to listen to your idea, even though you've got an unusual communication style or you don't have the credentials, then you'll go to that place. We were talking about Kariko earlier. She moved from Hungary to the U.S. specifically for these kinds of reasons. That doesn't change the fact that I think Europe is fundamentally a great place to do science and to do novel research.

If you take London, which is already an expensive city, it's still cheaper than going to the Bay Area. If you are in the rest of the world, coming to London is much easier than going to the U.S. There's no cap on the number of talent visas in the UK, for example in contrast to the U.S. We have unlimited willingness to take on really bright people. There's a long list of reasons why it makes sense to come here. Unfortunately, institutional diversity currently isn't one of them. And that's why I think it's a relatively small intervention that could make a very significant difference.

Samuel Arbesman:

That's really interesting. Do you think there's also other models of funding or tweaks on a venture capital that would allow people to do some of these interesting things as well?

Dominic Falcao:

I was thinking about this recently. Europe has a quite severe challenge, or the UK in particular. I found a statistic that basically alleged that the ratio of research funding in the Bay Area to venture capital was $1 of research funding to $15 of venture capital funding. In the UK, it's for every dollar of research funding, we have 10 cents of venture capital funding. See that as a blank canvas to create a venture capital industry for deep tech in the UK because we have to scale it 150 times, which means that you can't do it inside of the existing entities.

There's going to be new ways of doing it. Another point to make there is just that the only reason that's the case is because it's so expensive to build deep tech companies the way we currently build them. And we also need to find more efficient ways of building deep tech companies in the first place, which is one of the strong theses for DSV itself, but if we want to get there, probably, we have to do it in a way that's different from how the Bay Area got to where it is today.

I feel like one of the only ways of getting there in Europe is probably through family offices and through pension funds completely bypassing venture capital as a middle manager and thinking about direct strategies as an approach. If they were to do that, they don't have any existing answer to the question of how you navigate the opacity of science and the uncertainty of deep tech venturing.

And so, that requires the creation of new kinds of entity that could help them navigate that. So, I think there's really interesting opportunity in Europe to build the infrastructure to make what appears to be scientific risk more transparent to investors who are not perfectly expert in those fields. That's where things like the R&D co-pilot tool that we've been building, we've got this in-house tool called Elman, maybe the part of the wave of tools to navigate uncertainty for groups that don't have expertise.

So, how do you quickly understand what has to be true for a cancer therapeutics company to succeed if you've never invested in cancer therapeutics, and then how do you render into that framework a specific opportunity in the context of its peers? That kind of question, I think that we are in a quite good position to build completely transformational next generation approaches to navigating that uncertainty and facilitating capital at much greater scale.

We're not bottlenecked in the same way that the U.S. is by having very successful VCs, which have got a very strong brand in the same way that UK is maybe bottlenecked by having very successful universities. I think there are lots of great examples of VCs in Europe, but there's obviously space for more when you look at those numbers.

Samuel Arbesman:

You were mentioning this tool that you're developing, but going back to the United States and VCs, they are that intermediary that's acting as, I guess, in an ideal world, the intermediary and expert who can triage these things and figure out what actually makes sense and provide capital and direct it in the right way.

Do you think there should be VCs providing that similar role in Europe or is it the kind of thing that more family offices and pension funds should be doing that directly and use certain technological tools to make that kind of thing easier? Should there just be people who are providing this sort of thing as an advisory role, there's not as much of an intermediary to help bootstrap this kind of thing? I want to just better understand what you're thinking there.

Dominic Falcao:

I see VCs as a solution to a market-matching problem. They're pricing something that is otherwise very difficult to price, and they're using heuristics and pattern matching to do that. In deep tech, I'd say the market is more amenable to technological solutions because a lot of the problems are rationalizable in a way that, I think, in the history of consumer technology, for example, and B2B SaaS, they haven't been. It's extremely hard to predict the uptake of a SaaS tool by existing corporates.

It's relatively easier to understand the concrete thresholds for the performance of a cancer therapeutic or a new material, and it's much easier to achieve correspondence between performance in the lab and performance in an industrial setting for a new material than it is, for example, for a piece of software. And so, I wonder, and this is very speculative, if in achieving that leapfrogging effect, if the UK was to try and scale up its funding 150 times, doing it through the vehicle of creating new deep tech VCs, it's going to be constrained by talent.

It's going to be constrained by the conviction and track record of those partners. I wonder if a more realistic pathway would be to simply tackle head on the opacity of science and to try and render it into directly understandable metrics and thresholds and sub-outcomes and requirements, which you could then make investment decisions on the basis of. It's just more rationalizable as a space than investment has historically. It would potentially be a mistake to try and copy and paste this historic solution of how VCs worked onto the future of it.

Samuel Arbesman:

That's interesting. And so, maybe we can just jump more into yet the rationalization of this world or maybe using AI tools in science. How do you envision this? What would it look like several years down the line, these kind of tools are available? And then we can also discuss more broadly using AI for thinking about science and innovation more broadly.

Dominic Falcao:

I've been thinking about this a little bit thinking about insurance and how difficult it is to ensure novel technologies, for example. So, you have a similar problem, which if you overcome it for things like insurance, you could overcome it potentially for investment as well. So, insurance requires historic data sets in order to be able to understand future risk. And venture capital is similar.

We rely on patterns of founder-type behaviors and entrepreneurial behaviors in order to try and predict success in the future as the rate of technology development increases, so that pattern matching becomes less and less valuable and new forms of juristic are required. So, imagine that you're investing in climate tech today. Five years ago, it was a completely different set of technologies that we're doing direct air capture than they are today.

And they'll be different again five years from now. What we use today are things like technology readiness levels. We use the tenurity or prestige of the academic. We use how much research funding was spent on the research. These are all really bad measures. You want something closer to the actual functioning of the technology and trying to make a prediction of how it will work.

You want to know, does this technology have some chance of fulfilling this requirement in an industrial setting? In order to be able to do that, language models should be able to help us convert data from different maybe analogous technologies to this field. So, imagine, I'm trying to understand whether or not this electrochemical direct air capture system is going to achieve a 10X increase in scale from year to year? And is that a precedent to change?

Well, we can look at other electrochemical systems. We can look at, for example, the history of energy storage, and we can say, "Well, there was an electrochemical technology that had nascent manufacturing technologies that was able to scale those in some way." That is therefore analogous in achieving the scale jump from 1X to 10X.

This would be significantly better than using technology readiness levels because we're looking at constraints in shared areas, but it's very difficult for human beings to do this because it requires you to do pattern matching across multiple different dimensions across technologies that are only remotely similar across contexts, which are very different indeed, but you can start to see the picture of it as you think about it. In general, that's the way you'd want scientific investment to work is those uncertainties and those opacities eroded by the use of data from different settings to try and add some clarity.

Samuel Arbesman:

It also relates to the fact that, and I think, many times, investors can be blinded by their previous biases or what has happened the last time around when there was some boom-and-bust cycle, and they're like, "Oh, because it was like this and it didn't work, therefore this new thing might not work." And so, they become just jaded with the entire scene as opposed to taking a more principled approach which says, "Okay. Just because this thing didn't work doesn't necessarily mean therefore the entire class is irrelevant," or how to think about this thing even more broadly.

And so, it could be used as a way of both overcoming one's past history as well as allowing you to combine things together, overcoming these jargon barriers and understanding these things that, on the surface, might not necessarily be part of your area of expertise, but because these tools might have identified these things as particularly relevant when combined, then therefore they could be useful. Is that the way you're thinking about this?

Dominic Falcao:

Yes, exactly. I feel like when VC investors first moved into deep tech, they can't get around the fact that it didn't work in the past, so why should it work in the future, which is it works with consumer trends. We tried to persuade people to behave in this way, and they didn't. And that's a good precedent for future human behavior because humans didn't change that much in the last 10 years, whereas science did.

And even now, for science-specific investors, I often find that they will say, "I don't invest in this category because it didn't work in the past." They won't look at the specifics of what has changed in the intervening period. In fact, it's true for every single scientific invention that made it into the world, that it didn't work in the past before it works, right? That's the nature of scientific invention itself.

Samuel Arbesman:

Right.

Dominic Falcao:

And so, the nature of VC investment might need to change fundamentally in order to be amenable to this investment.

Samuel Arbesman:

In some ways then, and you mentioned having these tools and then them being used by non-experts, maybe, within family offices or pension funds, having someone who's maybe not as much of an expert, that actually could be a good thing. Would that be the most charitable way of describing this kind of thing?

Dominic Falcao:

Definitely true. I think it would be better if non-experts could appraise technical questions and understand the feasibility of scientific progress. It would be hugely beneficial for the world, in fact, if non-experts could understand the potential of science. And we would see what to be in a much greater allocation of funding into early-stage innovation, if that was the case in my view.

Samuel Arbesman:

But of course, I think this kind of approach, it only works for one category. I wouldn't necessarily one category of deep tech startups, but certainly one way of thinking about scientific innovation, and I would say more in terms of how to build a startup that can be funded and scale rapidly without too much scientific or engineering risk because I imagine this kind of thing would not work as well for figuring out how to allocate resources for fundamental scientific discovery, one, because it can be a lot more undirected or it's very hard to understand where things are going to go, and also just the fact that, ideally, science, to a certain degree, is a public good and therefore should not be funded by venture capital or things like that when it comes to the more fundamental research. What you're saying is this kind of approach is only going to work for a certain type of science in this case, a specific category of funding deep tech startups?

Dominic Falcao:

100%. In fact, I think allocation of the funding into scientific questions should allocate in the exact opposite way. So, you want to allocate funding to areas of the greatest uncertainty in science, whereas with technology and technology that is derived from science, you want to allocate into the areas with the least uncertainty. So, with allocating it to science, you want to ask what are the questions, which, if we answered them, would represent the greatest Delta on what we know, which is very distinct from when you invest in technology.

Where you're asking technology is what's the allocation, which, if made, would give us the greatest Delta on what we can do? They have really different questions. And you can't tell what you can do unless there's low uncertainty. So, there is a lot of space for thinking about greater intentionality in science funding and research funding, but I don't think it's about shying away from uncertainty. I think it's about trying to come up with measures of importance.

Is this question important for science? Does this represent potential learning about a large number of different fields that are interrelated? And a lot of learning about each of those questions, which is a possible gauge of importance. And it's not the gauge that we use today generally. I think there's a vast amount of improvement for those kinds of mechanisms on the science side, but I just think it points in a diametrically opposite direction from the technology arrow with respect to uncertainty.

Samuel Arbesman:

And that reminds me actually of an essay that... So, Ben Reinhart, the head of Speculative Technologies, who we actually had on the podcast a while back, he wrote this little essay a couple of years ago with the title, When Should an Idea That Smells Like Research Be a Startup?

And at least in my reading of it, the answer is almost never, because when you have not de-risked a lot of scientific ideas or things are more undirected, these things are really, really valuable for moving science forward and eventually moving technological advancement forward, but to do them all within a startup is not only really hard, but almost like diametrically opposed to the kinds of things that deep tech startups are.

Yet, to what your point is, right, there are things that deep tech startups are really good at doing, and then there's also things that scientific advancements are really good at doing, whether it's within universities, whether it's within all these other different types of organizational structures that we've talked about, but to try to shoehorn everything into the startup structure is almost like a category error.

And so, yeah, right, you have to be very open to figuring out, okay, how do we think about this thing, how do we think about the tech trees, how do we think about where our uncertainty should lie and how it should work, rather than saying, "Okay. No. This stuff is really cool. Let's just fund it all like a startup," because then, I guess, therein lies trouble and madness.

Dominic Falcao:

The words category area were in my head as you said them because I was thinking about the decision or the perception that science commercialization should rest with universities as a responsibility, as a kind of category area. That's very similar in its nature in a sense that because people at universities understand the science, they should be responsible for the science commercialization, but that misconstrues science as being some kind of linear process where we understand something, we produce some knowledge, and that knowledge then needs to be considered for its possible applications, which, for almost every kind of knowledge, are underdetermined.

So, just coming back one last time to the Kariko, for example, realizing that pseudouridine is going to help you reduce inflammation from mRNA vaccines or mRNA in general. That could apply to cystic fibrosis. It could apply to cardiovascular conditions. It could apply to neuronal conditions. It could apply to any number of things before you settle on it being, for example, vaccines. I think they also looked at cancer for some time. And so, that question of, well, is there a more efficient search problem that we could use?

It's looking at the science from a different lens, which is going to give you a more constrained search algorithm. It's going to look for the set of things which achieve specific solution rather than the possible applications of given technology. That's the way I think about whether or not this fits inside a company is did this company conduct a search to understand whether or not this set of components together represent the lowest uncertainty way of achieving the outcome they're achieving?

So, very often, if I have a deep tech company pitch me, I will ask them the question that, given the specific solution or outcome they're trying to achieve, what set of different disciplinary approaches that they consider in getting to that same pathway as competitive? Because if you're a biology company working on wastewater treatment, you're competing with thermochemistry. You're competing with mechanical engineering. You're competing with electrochemistry. You've got a whole host of different completely orthogonal pathways to that same solution that it's highly unlikely you ever considered.

Samuel Arbesman:

And it is, unfortunately, the answer often. The major thing I considered is the technological advance that I happen to be involved in actually developing. Is that often what happens?

Dominic Falcao:

Yeah. And it's a really brutal moment because that finding, that understanding, that piece of knowledge this person's come across, it almost certainly does have societal utility.

Samuel Arbesman:

Right.

Dominic Falcao:

It's just that they need to be met by someone coming from the other direction.

Samuel Arbesman:

Right.

Dominic Falcao:

And if these two arrows are pointing in diametrically opposed directions, then you need someone coming from the other direction, but we don't have, if we're talking about the need for new institutions, sufficient institutions or sufficient funding pointing people back from the desired solutions towards the scientific landscape. So, that that person coming out with, "What can I do with my technology?" is met by someone saying, "I'm looking for something that fits that box in my requirements graph."

The more often that happens, the better the solutions you get, the more efficient the process of science being translated into impact, but the problem we have at the moment is that we fixate on universities as a bottleneck when, in reality, we've talked earlier on about UK universities being just as efficient as US universities. It's not the bottleneck at the university. It's the bottleneck at the matching between what we know and what we want to be able to do.

Samuel Arbesman:

And so, going back to AI, do you think AI, long-term, will be an enabler in helping with that matching or even at the more fundamental scientific discovery state, helping researchers expand the space of the different ideas they should be considering when they combine them together in terms of making an advance? Is that something you see going forward as well?

Dominic Falcao:

That's one of the things we've been trying to do with Elman is when you first open Elman, and you start interacting with the R&D co-pilot, it asks you what the target outcome you're trying to achieve is. You can't get past the first question before it's asked you what you're trying to do. It is possible to do, "What can I do with this technology?" but just as it is with an expert trying to do that. Tech transfer executives are not stupid.

They're just doing one of the world's hardest jobs, which is navigating the future possibilities of a piece of knowledge. It's like trying to make investments in a company when all you can see is a technology slide. So, what co-pilots like Elman may make it possible is for scientists themselves to have this tool in their hands and to ask sooner on what possible applications could I do? Okay. Picking that application, what would have to change about my scientific pathway in order to hit it? And what are the requirements for a commercial application of this technology? Is this the most efficient route to doing it?

So many of the scientists I've worked with, the number one reason they're in science is for impact. And so, putting the pathway to impact back into their hands is something that is on the net of horizon through our R&D co-pilots, and one of the possibly greatest, most game-changing changes that a way that we do science commercialization and moving that arrow into their view and giving them that lens on their scientific research earlier.

Samuel Arbesman:

That's amazing. On that optimistic note around changing impact, that might be a great place to end. This has been fantastic. Thank you so much for taking the time to chat with me.

Dominic Falcao:

Cheers, Sam. I really appreciated it. Good conversation.

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