[0:00] what is your research aboutHello, the guest today is Buzz Barstow, PhD, class of 2009, and he is currently a professor at Cornell University. So hi. Hi Buzz. What is your research about? First of all, hi Tony. It's always great to speak with you. I always, I always really enjoy it every time we talk. What's my research about? It's about building sustainable energy technologies with synthetic biology, but it's also about understanding the basic science that we need to build those technologies as well. Interesting, So like what are examples of something that you would build? Yeah, we, yes, we do. I can give you a couple of examples. I'll give you 3 examples of our work that have really taken off since since I came back to Cornell, and I'll go right back to the beginning. I think this is really important, that if you were a PhD listening to this, I'd stressed, I'd really stressed to you don't think about the money or at least think about, you know, Yeah, yeah, think about it, right. But the first thing you should really be thinking about are interesting problems. And you shouldn't, you shouldn't pre constrain yourself by thinking about what's fundable and what's not. You should never think of science as the thing that you can get funded, especially by the government. You should be, you should be thinking sort of what's interesting, what's interesting to you. You know, what might, what knowledge might you unlock that's good for the good, for the public, good for humanity, what's beautiful? You know, what's true. You should really, you should always be thinking about that first. And then once you know, once you know that, once you figure that out, you should then only then should you think, how do I convince somebody to pay for this? Don't think about, you know, the money is secondary, right? As important as it is, and I was really lucky, actually, I was really lucky as a as a grad student at Cornell, I never had to worry about money. My PhD advisor, a Sol Gruner, always seemed to take care of that. I did a very good job of it. And he was able to, you know, seemingly able to figure out how to pay for things that were very interesting. I don't know how he did it and but you know, when you think back, you're like God, how did he, how did he get the money for that? So that way you could focus on the interesting problems. Exactly. And not, and not just the interesting problem of my, of my PhD, the kind of interesting problem of like, what did I want to do with my life? Like what was a worthwhile challenge to go after? And I knew that I, you know, I think I'd intuited that for a long time. Biology was going to be a really important part of technology of the 21st century. I think I watched a documentary when I was a kid and it said that physics is the, you know, preeminence was the preeminent science of the 20th century, but biology is going to be the preeminent science of the 20. I don't know how much I, I internalized that at the time I, I did my undergrad and my PhD in physics, but that I definitely was always at the back of my mind. I, I, I worked for a startup company. My interest in startups, you know, it started when I was a kid. You know, my, my dad was a, was an entrepreneur and one of my advisors, John Hazard at Imperial College was the first scientist I ever met here at a company. He had AI worked. You know, I I paid my way through college working for companies and I got a job at his startup and it was a biotech. And I thought like, this is this is kind of the physics and the biology I want to do. And so, you know, throughout my PHDI was looking for a problem and, you know, a big problem that we could, you know, that would be amenable to solution with biology. And Hurricane Katrina happened and I thought, God, that's, that's the problem I want to solve climate change. You know, I was very lucky that, you know, as a PhD student, I had an awful lot of freedom to think about this and, and to think creatively about like how biology might be used to solve that problem. I asked Saul, you know, how do you know, how would you go about funding this? And they said not not totally sure. I think he was right about that. You know, it's not trivial, but somehow, you know, I've, you know, been able to figure it out. And then I, I remember reading in a book that Saul gave me, or, you know, told me to read it. And it said that, I think I'm paraphrasing a little bit, but it said that thermodynamics owes way more to steam engines than steam engines do to thermodynamics. It introduced me to this idea that there's this interplay between science and engineering when both are at their best.

[5:26] getting started in synthetic biologyI then I went to Harvard Med School as a postdoc in synthetic biology. And what I discovered there through, you know, a lot of stuff not working was that biology, that synthetic, that sort of synthetic biology is not yet really an engineering discipline in that we don't really understand all the, the fundamental science behind it. And we don't have rules of thumb really to replace those. So, and it's, and it's sort of sourced. The first example I found of this was aviation in the late 19th century, very early 20th century. And the Wright brothers, they realized that, you know, there was a body of literature on aerodynamics and it empowered flight, but it wasn't, it wasn't very extensive. They, they set about testing its assumptions and the results of, you know, its implications. And they quickly found out that the, they quickly found out that the sort of the fundamental science of aerodynamics, I think Leland, I think it was Leland Tall's equations, I think they weren't right. You know, they didn't predict the sort of, if you, if you have a given wing shape, Leland Tall's equations predict a certain amount of lift and you know, a certain amount of dragon, you know, the width, you know, if they actually measured this, well, it was, it was too much dragon, not enough lift. And as a result, you know, they could have given up, but they, they sort of had a brain wave and realized, wait a SEC, we could build a wind tunnel and we could actually test all of this systematically very quickly. And you know, I think I'm a little, I'm a little fuzzy. I think certainly within 18 months, maybe within six months, they had a working, they had the, they had the first flyer. Interesting. And I realized that biology is, is sort of in a similar situation. Synthetic biology is in a similar situation, especially with regards to applying it to sustainability. And so I, I realized, wait, we have to do this sort of hand in hand. And I was, and, and you know, my one, one of my first goals I realized when I was a postdoc, something that was great about it was that I sort of got to think again, think deeply about, you know, where, where in where can we use biology? What are the big problems in sustainability? And one of them was, um, you know, if you think about it, if you are going to use biology for sustainability, you need to power it. And the way we power it is through sugar. And sugar comes from photosynthesis. And it turns out it operates an enormous scale, but it's phenomenally inefficient. And so I said, OK, a big goal of my lab is somehow my career is going to be figuring out how to make it more efficient. And there's a few different ways of doing this. The way that we hit on was to to sort of get rid of leaves and replace them with solar panels. Solar PV is incredibly efficient and it's getting more efficient. It's getting cheaper every year. Could you then take that solar electricity and use it to power metabolism? And it turns out maybe is the case. We know there are microbes that can absorb electricity into their metabolism. The only problem is we don't know how they do it. Well, we didn't know how they do it. And as a result, we didn't know how efficient this process could be, especially on a sort of energy conversion basis. So was it worth investing, you know, maybe years of research, years of engineering, the people's careers, lots of taxpayer money into this. And so I, you sort of said, gosh, you know, first thing we've got to figure out is how this works, this interface between electricity and metabolism. And I, I've realized that the sort of the genetic tools that we've got at our disposal at the time sort of suck and I would need to come up with better ones. What I realized I needed was to be able to systematically knockout all of the genes in an electroactive microbe. The one I chose was Shiwanella at the time, and probably still is the best known electroactive bug. And I thought, well you know this. This technology exists for yeast and E coli, but it takes years to knock out all the genes and it costs millions of dollars. And I have neither of these things. So Michael Bame and I Michael is now an associate professor at Harvard Med School. We came up with this technology called knockout Sudoku, which allows us to knockout all the genes in a genome. Instead of costing millions of bucks, takes about $10,000. Instead of instead of, you know, costing millions, it costs 10,000 bucks. It was right. We came up with this at the end of my time at Harvard, but I was able to my, my wife got a position at Princeton and I was really lucky to get a fellow position at Princeton. And they, they sort of took me on and I was able to make the Sudoku technology work there. And that was with that, what we were able to do was build this knockout collection for Shiwanella and then screen it for the genes that controlled electron uptake. And with that, we were able, me and Annie Rowe, who is now a professor at Michigan State, we were able to figure out this electron uptake pathway. And and because we knew it's mechanism, we could then calculate a theoretical maximum efficiency. And if we could do that, what it told us was this is really worth doing. It told us this could potentially be incredibly efficient. Did you have like 10 different experiments at the same time and this is the one that ended up working out? Where were you? Where was there a lot of clarity from the beginning that this was the path? Like did you? Have. Yeah, Yeah, it was. It was, God, that's a great question. It actually kind of became fuzzy sort of midway. Actually. I think I tend to dive into things and like, become like be quite obsessed with them. I do think I probably, you know, I probably can be accused of falling in love with my own ideas about midway. I realized, you know, this is way harder than I thought. So it forced me to say, OK, well, the first question I asked is, is, is, you know, going after problems in sustainability even worth doing? I actually, I remember like thinking, God, you know, maybe maybe medicine, you know, biomedicine is of the right way. Maybe that's like maybe, maybe I've got it all wrong. You know, maybe everybody else is, you know, doing the right thing. I do think I'm like a little bit, I wouldn't say a contrarian, but I do like to do things that are different from anybody else. But I remember I was sitting in this, uh, this coffee shop across from Harvard Med School with a stack of books on medicinal chemistry and Uriel on who is one of the founders of systems biology. He was a he was a visiting professor at Harvard Med School at the time. And, and he asked, he saw me, you know, I probably looked bored out of my mind. And, you know, he saw me. And he says, you know, let's play a game. And this is a really good exercise in like trying to figure out what you want to do in life. And he says, you know, think about what you know, you know

[13:16] what makes a research problem interestingwhat, what excited you about science as a child, right? What got you into it and write it down and then say, OK, and then formulate what you're doing. You know what you're going to do next. That sort of hits, you know, kind of hits all the same notes, pushes all the same buttons for you. And I, I realized what, you know, what I'm doing with sustainability and and biology is exactly what I want to do, right? Like, and I should persist with it. What I did realize from that conversation and later on when I was looking for a faculty position was that it's not clear to me that any single approach, you know, any single technology that we could make out of synthetic biology and, you know, for sustainability is going to work. And we have to come up with a portfolio of ideas. You know, if, if somebody's going to fund us, then we really do have to, you know, especially like a university is going to back you. You do have to sort of, you know, spread the risk around. And so I came up with this portfolio when I was at Princeton. I, I came up with this like portfolio of ideas about where we could apply sustain, you know, energy, you know, synthetic biology and energy. I wrote an article about it with Jose Avalos, who is a, a very good friend of mine at Princeton. And then I wrote a job proposal about it. One of the ideas was biomining, using engineered biology to get all the metals we'll need for the sustainable energy transition. If you think about it, we want to get away from fossil fuels. And one of the ways that we're going to do that is by electrifying everything in our economy. Cars. We're going to replace the electrical distribution grid perhaps with superconductors. We're going to have heat pumps instead of the boilers. We might have electric aviation even. And this is going to have a tremendous demand for metals. We thought, well, mining is horrible. And if you think about mining, the mining of a lot of these technology critical metals has been outsourced to developing countries, China being the most prominent example. And this is not great for two reasons, right? Like one, it's sort of it outsources the negative externalities of mining. Some people call this like eco colonialism. And the second is it gives countries like China, maybe Russia, South Africa, it gives them geopolitical leverage. It's like we've traded our addiction to oil. We'll trade our addiction to oil, which comes with all sorts of political complications to an addiction from metals, which will just come with another set of political complications. So it's like we're not really any better off than when we started. Maybe we are, we are in terms of the environment, but everything else we're, we're not, not in much better shape. I thought, gosh, is there a way to do mining better? You know, there were when I, you know, when I started this in 2016, there were a handful of scientific papers on this. You know, none of the microbes that existed at the time had had like anywhere near the performance that you would need for a viable industrial process. I said, wait a SEC. If we could, if we could figure out the genetics of these processes, maybe we could improve them through genetic engineering. And that, that idea is what me what got me my job at Cornell, actually. And the, the bio mining really sort of, you know, that was the thing that, you know, people just got it right. You know, it's, it's hard. The the microbes that eat electricity is this. Yeah, with, with the Sudoku technology. Yeah, the microbes that eat electricity thing that's, you know, that's hard to get right. But the, you know, bio mining people, it really resonated with people and it proved it was like incredibly easy. It wasn't incredibly easy, but it was way easier to fund than bugs that eat electricity. And, and we didn't look back from there. It was very easy to recruit talent around the idea as well. Alexis Schmidt I remember I was very lucky. I met my first postdoc, Alexis Schmidt, at a seminar I gave in plant science in my first year for now. And she she became my first postdoc and she used Sudoku to figure out the genetics of a microbe called Gluconobacter. A few years earlier, a group at Idaho National Lab led by David Reed and Yoshko Fujita had figured out that Gluconobacter was almost good enough to build a bioprocess for mining rare earths just wasn't quite good enough. And so we said if we could engineer it, we're we'll be in business. And so Alexa figured out how to engineer Gluconobacter to make it better. At the same time, one of my grad students, Sean Medine, also used Sudoku to figure out the genetics of selective biosorption of lanthanides. If you think about it, there are two problems in bio mining that or in mining that you need to solve. 1 is getting minerals, getting metals out of a rock that's extraction and then there's no rock that has just one metal in it. When you dissolve it or leach it, a soup of metals comes out and you then need to separate each individual metal from the soup. Lanthanides, or you know, the rarest are, you know, that's an extreme problem for them where they're all very chemically similar, and so you have to use very extreme chemistry to separate them. A few years, you know, again, a few years before I started my position at Cornell, a pair at Harvard, Beneficial and Clark had figured out that a few microbes, Fuenella was one of them, could do this. They could selectively bind. Lanthanides potentially could be used to separate them and they showed that under some conditions this separation process was almost as I think almost, if not slightly better than a conventional solvent extraction. And so we said, could we, Could we again? Could we engineer Shiwanella to make it leapfrog conventional technologies? Which dimensions are you working on like? Which dimensions you work on like? Is there like better in terms of like faster the process, easier to do, less cost to do it, less energy used? Like what dimensions is the better? Oh. My gosh, that's a great question. The ones I was, the ones I was thinking of. Yeah. Yeah. This is going to sound really silly, like, like, so, you know, probably I think somebody else could give a more intelligent answer. We just wanted to make it like less environmentally horrible. So of coming back to that specific example of separation of lanthanides, the the metric there is number of separation steps. Gotcha. So each separation step would have byproducts that were bad. Yes, exactly It would, it would use solvent that were nasty, you know potentially carcinogenic. And if you could do, if you could do it with a bioprocess, you could just do it under a quiz conditions. Gotcha. Interesting. Coming on so So Sean figured out how to engineer Gluconobacter shiwanella and then later a bug called Vibrio nitrogens so that it would have dramatically better biosorption characteristics. Alexa engineered Gluconobacter so that its ability to extract rare earths was dramatically better. And this work was funded by, you know, first just by my start up, then Cornell Atkinson helps us out, and the Cornell Energy Systems Institute, then we then ARPA, the Advanced Research Projects Agency for Energy, gave us like, most of our funding throughout the pandemic. I'd always wanted to, you know,

[21:51] startup brings tech into the real worldstart companies because I figured we'll only make the world a better place if we can get this technology out into the real world. And to do that, we need to start companies. And Sean, Sean really wanted to do a company and he knew that from as soon as he got into grad school. And so we are we, you know, we, we have this sort of agreement. He would take it and run with it. Rex also really wanted to do a company and they started regen together. Regen is, you know, regen is is sort of left my lab in. Alexa graduated or graduated in 2022 with the help of a an activate fellowship from the Activate Foundation and they also got support from Cornell. Alexa won the, I think it was the women, I think it was the women's Innovator award from Cornell Tech Licensing. And they started, they, they got incubator space in the Praxis Center, which is the, the physical sciences startup space. I think. I think in the last year they moved out to, they moved out to Langmuir, which is by the airport as they've been scaling up. Also, Ian Brooke was my first lab manager. She and Alexa are great friends. And Brooke became like a vice president at Regen when, you know, when they graduated. And it's, you know, still with Regen today. Coming back to bugs that eat electricity, we realized while all the rarer stuff was happening, we realized that we were trying to make this bug. We'd figured out that bugs that eat electricity and fixed CO2 could be really efficient theoretically. And yeah, we were trying to make it. There is no bug that we were aware of that, you know, could eat electricity, fix CO2 and could make jet fuel. So we would, we'd have to make it through genetic engineering. And she, when Ella, you know, she, when Ella is like genetically engineerable, but it's a, you know, it's a pain in the neck. And everybody I know who's worked on it has gotten put on a 26 hour day and has gone slowly insane. And so we, we, we thought, you know, we can't, we can't be having this. So one of my postdocs, David Spect David, if it is another Cornell alarm, he was applied physics PhD and he had, you know, we realized that we needed to swap for something else. And we hit on this microbe called Vibrio nitrogen, which is it's one of the fastest growing organisms on Earth. And it's it's the fastest growing Organism you'd actually want to work with because it won't kill you and it doesn't stink. And we also realized that if we're, you know, if we're going to engineer it so that it eats electricity, we discovered that it actually probably can eat electricity. It's got all the genes that you need to do that. If we were going to engineer it so that it can fix CO2, we later discovered it can also. It can probably fix CO2 as well. But if we're going to engineer it to make like the CO2 fixation and the electron heating and the making of stuff really efficient, we're probably going to have to radically edit its genome to do that. We don't have a prescription for how to do that. We would have to do that through directed evolution. And the challenge there is that that sort of traditional approaches for genetic engineering don't seem to work very well for autotrophic metabolism, for bugs that are fixing CO2 rather than eating sugar. Ron Miller, Ron. Ron is a professor at the Weisman in Israel and he he'd actually been able to build a strain of E coli that fixes CO2. And he managed to do this after I think a decade in 2019. And it's probably one of the greatest feats of synthetic biology like ever, you know, to date. But it took him months and months of directed evolution to do this. And the the resulting bug is still very slow wanted. We want our bug to work incredibly fast and incredibly efficiently. And so we we can't rely upon random mutagenesis to do it. We we realize that we would need a much more targeted method of mutagenesis and there are methods to do this for heterotrophic metabolism. The best example I can think of is called MAGE. That was developed by Harris Wang and Faron Isaacs, who were then in George Church's lab at Harvard. And we realized this. This won't work for autotrophic metabolism because it relies upon a process called electroporation, where you get DNA into the cell by zapping it with electricity. And this is really bad for the cell and you need a lot of cells as well to make it happen. And David realized, wait, maybe we could circumvent this by we could circumvent this by using a process called natural competence, where a microbe, most microbes it turns out, actually do this. And E coli is actually an outlier in not being able to do this. It can take up DNA through a molecular process rather than a chemical process. So it can do it at very low cell density and it can do it without the recovery periods that E coli needs when it gets zapped electricity. And David made this work, right It you know, it turns out that a lot of people have been trying to make this work and David was the 1st to get there. This is fled David and Bryce

[28:06] staring a second startupBrownfield and Cameron Kitzinger. He worked a three alumni of my lab to start a company called Forage Evolution to further develop this. They're based again, this comes back to sort of all the support, right, that Cornell sort of has has given us, right? Like when I started at Cornell, I was a grad student like you mentioned. And I felt that at the time, this is like 25 years ago that Cornell was kind of ambivalent to companies. And now I feel like that has completely reversed. And I feel like there are all these opportunities for doing companies and, you know, for people to stay in Ithaca. And. Forage is based at what's called the Center for Life Science Ventures, which is like a biotech incubator on Cornell campus. The last thing we chatted, we talked. About the Stokes model of research funding research, like how does the how does the commercialization process fit into that Stokes model of research? Oh my gosh, that's a great. Question So Oh my God, that's a great question. So I'm going to illustrate this was an example. So I real. So I realized, OK, we've done the rare earths, right? And that that was what created regen. But there are all these other rare earths or sometimes used as like a catch all term for, you know, all these elements that we're going to need for sustainability technologies or defense technologies. But actually it's just a little bit of the periodic table. There are there are probably 25 other elements that are essential, technologically essential, but how of vulnerable supply chains. And we, we figured we wanted to bio mine all those other elements, but we didn't really know where to start. And, and so we realized, you know, what we need to do is create new fundamental science in order to build these bio binding microbes. We need new science in addition to genetic engineering. And this is, you know, up until very recently, this has been a real problem to do. This has been really tricky to do. So for the listeners, I'm going

[30:27] research funding and innovation frameworkto explain the the Stokes model. So the the way that science is funded in the United States originated sort of in the aftermath of World War Two in a report to the federal government called The Endless Frontier written by Vannevar Bush, who was the president's first science advisor. And he lays out this idea that that if we, you know, if we do basic science, you know, curiosity driven fundamental research, you know precisely what fundamental basic research means. It's a little bit in the eye of the beholder, but you sort of know when you see it. Bush argued. If you do this, if you sort of build up this knowledge bank, you know, he called it seed corps of science, you'll get transformative technologies out of it. And this this idea has sort of given the scientific community, you know, it's allowed it to, you know, take federal funding, but has allowed it to operate quite, you know, an arm's length from the government, you know, with a fair degree of independence. But that model about 50 years after endless frontier. Yeah, we, we were the scientific community. We're starting to realize, well, you know, maybe this is not quite right, and historically, science and engineering actually go hand in hand. Mm. Hmm. If you if you know it. Let's say 25 years ago, if you were to, or even a decade ago, maybe even five years ago if you were to propose to the to a government Funding Agency that, you know, we're going to discover this. You know, we want to make this microbe that mines germanium or antimony, but we don't know the science behind it. We're going to figure it out. We're going to figure it out and promise and then we're going to engineer it. He would have been greeted with a great deal of skepticism that the scientific. They would have said, well, you know, you know, this is, you know, if you went to an engineering agency, Department of Energy, I think perhaps being the best example, they would have said this is a bit too fundamental science. And if you, on the other hand, if you'd have gone to the National Science Foundation, they would have said, well, wait, no, this is this is too engineering, you know, or it's just boring. It's it's, it's kind of in between. Or if you'd have gone to the National Institutes of Health, they would have said, well, it's not medical, so we're not funding this. And so you would have been left, you know, without many options about how to fund this. Don't realized this problem almost 30 years ago. He wrote a book called Pastor's quadrant that sort of outlines this issue and he makes and he makes this great point that if you think back to the the sort of great inventions of the past and he brings up Louis Pasteur, the French microbiologist as a as his sort of exemplar. He says pastor's work. If you think about it in this one-dimensional model of science, it's neither applied nor basic. It's sort of in between. And if you think about in that one-dimensional framework, it's, it's kind of boring. You don't really know how to how to sort of categorize it. But wait a SEC, what if you think about this in 2 dimensions, consideration of use, which is high, and quest for fundamental knowledge, which is also high. And what this reveals is that Hasta's work within a was in a totally different sort of space from let's say general relativity, which is purely curiosity driven. It's very fundamental and say engineering light bulbs or engineering integrated circuits. And if you, if you don't look, you know, go look through the history of science and technology, you find several examples, a lot of examples like this, for instance. You'll find the. Discovery and harness exploitation of antibiotics. You'll find solid-state physics and the creation of the transistor. You'll find aerodynamics aviation like the Wright brothers who I mentioned earlier. You'll find the creation. Of dwarf wait. And most recently you'll find things like mRNA vaccines and very few of these inventions, these kind of great inventions were funded by government. And I think that when when Bush wrote the Endless Frontier, I think he sort of came up with this paradigm, as I understand it, because he wanted to protect the he wanted to protect the independence of the scientific community. I also think that he understood that at the time that a lot of this use inspired fundamental research was done by by private organizations in America and and especially in Germany, or had been done by in Germany before World War 2. Before the. Nazis destroyed the German scientific system and he thought, you know, Bell Labs is is doing this. We don't need to worry about it. But you know, as as say Bells monopoly was was eroded and eventually dismantled. Probably a good thing in many ways. Bell Labs also, you know, the funding for Bell Labs was, was eliminated and and so there was no place in America where you could do this sort of use inspired work, probably no place in the world. And so it makes, what this means is I think that it's made creating very new sort of fundamentally new fundamentally new technologies. It's very, very difficult. And you can sort of see this in our rate of economic growth since the 1970s. Is it the? Issue now that is the reason for this is that because there's just so much more scientific knowledge and so much more engineering that it's hard for one person to know the full breadth, like the full stack of it. So that's why people are specializing in one or the other. Like how does 1 become a good four step kind of person? Oh my gosh, that's a great. Question that's a deep question.

[36:54] how to good at use-inspired researchI, I, I don't know to be quiet. I think this so actually the, this concern about specialization is actually a perennial 1. I know Bush himself worried about it deeply and he, he actually wrote this very famous essay called Oh my gosh, I'm blanking on its name. I'll send you a link to it once we get offline. But he sort of predicted hypertext in the 1940s, and he sort of, he wanted to build a sort of information retrieval system that would allow people to break out of this specialization trap. And people like Licklider and Doug Engelbart, who later went on to work on like human computer interfaces for Darker in the 60s, read this and we're like, we're sort of inspired by it. And so I definitely think the specialization is part of it. I don't think it's the whole story, though part of it might be the. Say the National Science. Foundation or the Department of Energy, they like funding curiosity driven basic research. Starting in the 1970s, you know, people rightly became very worried about things like DDT, nuclear war and they said, wait a SEC, we, you know, wait a SEC, we just want to slow this down a SEC, right? Do we really want to be building new technologies like say the atomic bomb without really thinking about it? And what this might have done is, is sort of reinforce this preference for sort of just purely curiosity driven basic research in the funding agencies and the review process thing. And and as a result, the sort of use inspired basic research that's needed to build new technologies. Just, you know, didn't was hard to fund and, and, and maybe people respond to the career incentives and all like, OK, well, I'm not doing that because I'm, you know, I'm not, you know, they're want to have a career. I totally understand that. I think in. Many ways I've. I've sort of been very lucky to, I don't know, sort of been slightly insulated from that. And, you know, just by luck, I think, or maybe my temperament, I think that I wouldn't want to claim that I, that I fully understand that. I think to do so would be, I think, a little bit arrogant. And I, and I think that I definitely think that the world desperately needs new technologies today. And, and I think, I think that the reason that they haven't shown up, there's this, there's this great book called Rise and Fall of American Growth, and it documents this sort of like slowing down in the rate of, you know, productivity and economic growth. In America and, you know, other advanced nations, yeah. The, the, the sort of the hypothesis is that there were these like great inventions of the 19th century, you know, like, like, like electricity, you know, 20th century to antibiotics, Right. And you can sort of read it. I'm rereading it at the moment because, because I want to see if I really understood it the first time I read it. You know, I, I don't want to like disparage it too much because it's like, you know, it's, it's a really amazing book. But like, you know. They, they sort of make this claim that, you know, those things were like low hanging fruit. And I'm like, wait a second, like, let's just say from the perspective of, you know, 1770 was, was electricity low hanging fruit? And I think to say that would be to, would actually be very arrogant. I, I think it would, it would be to diminish the, the genius of the people who figured it out, you know, the Ben Franklins, the Faradays, the Maxwells of the world. Likewise, you know, if you were to say from the perspective of like, you know, 1600 or certainly 1500, it was gravitation and classical mechanics was, was that low hanging fruit? I don't think it was. I mean, I mean, you know, most of human history went by without, without any of this stuff being figured out. And, and just to say that it it's kind of only low hanging fruit in hindsight, I think. And so there may be fundamental science that we have yet to unlock that could unlock new technologies. And we sort of haven't. Unlocked it not because. You know. Not because it's just fundamentally more difficult than the science that we've already figured out, but because something about our societal arrangements is getting in the way. Maybe we slipped. Back into an older mode or something like that, more kind of risk averse, conservative mode. I studied applied engineering. Physics at Cornell, I really liked how it was like the physics, like you learn a lot about like quantum and electromagnetism, but you also learn a lot about the engineering implementation of it. Is it like studying like something like AEP? Would that, like, help train more people to become more like pestors? Oh my gosh, yeah. I would love.

[42:41] applied and engineering physicsThat, I mean, if you think about like AEP is like one of the kind of jewels in the crown of Cornell, right? It's like it's one of the yeah, I know it's like one of the one of the. I say this is an anep. I love it as well, right? Like so, but like, yeah, I kind of think it would like. I think that I think if you think about it right, like ANEP kind of, I would say it, it came about because it, you know, it, it, there was an academic department that wanted to exploit the potential of solid-state physics. And I think you know it, correct me if I'm wrong, but like that's still its focus today. It's like optics, solid-state physics. I would love it if there was and and in many ways Bea is that department for sort of synbio and and sort of sustainability, right where there's an engineering and the fundamental aspect do it yes yeah. So so like if. Someone is if someone is like starting like at Cornell now or is like thinking of doing a PhD, how could they think more in terms of curiosity but also use considerations too? Oh my gosh, that is a great. Question, I would say, my gosh, that is a really, really great question. I would say if you were, if you were starting out, I think there's loads to be figured out in biology. I really do. I would. Urge them go into biology. I would actually, I would really, really encourage more people who did did an undergrad in physics or applied physics to get into biology as well. Massively, massively. So it would, yeah, I would really, really strongly urge them to take a look at it because I think that your skills in like sort of your quantitative skills are desperately needed in biology and also come in like I would absolutely, absolutely come in with a bit of humility as well. Because you get deeper into. Biology that, that biologists have a wonderful complementary skill set to physicists. And I can only describe it as being like, like a green thumb. And there are people in the world who can make anything grow and they have like an, A sort of an intuitive sense, at least I think it's intuitive of, of sort of how to work with, with living, living things. I don't really have that actually, I've got to say I've been very lucky to have found people to work with who do, but I don't have it myself. And I would urge you to have, if you're a physicist, right? Have humility about that. Recognize that there are things that biologists can teach you and there may be things that they can do that you just will never do. And you know, you've just got to partner up with them. But I would strongly encourage, I would strongly encourage if you were a, if you were a junior or a senior in, in physics, come, come take a look at biology and I think you would find a lot that you could contribute to. Yeah, as far as I'm thinking. Of like the uses like the engineering uses of biology, is it like choosing an advisor who is doing commercialization as or do you take part in more industry conferences as well to understand the uses of the science? Oh my gosh, that is a really good. That is an awesome question. I think, gosh, I think when? I think when picking your. Advisor, you sort of, you know, I think it's a very personal choice, right and. I would, I think. It's important to recognize that no advisor or very few, Maybe not, maybe not all, but you know, very, there will be very few who do everything you want to do right. And as you get older, right as you go through your PhD, what you want out of life is going to change as well. When, when you're looking for an advisor, you know, you want to work with somebody who you can just have a dialogue with, I think, you know, is doing something generally interesting. And as your PhD goes on, you know, I think if that first condition, you know, your advisor is generally flexible, you can figure out everything else. I think. I think if you do want to bring your work to the real world, out into the real world through engineering, it does help to have, it does help to have an advisor who is sort of thinking about that, who sort of has that, you know, that kind of use inspired mindset. That being said, you know, that is, I think that is a mode of doing science that we're sort of relearning how to do. I couldn't claim. That anybody does it perfectly. So, so don't, don't go looking for perfection. I would say you might not find it, but but but I would, I would sort of, you know, you're going to find people who are more amenable to it than others, I'd say. And yeah, that makes sense. And then how about like on the institutional level, like the college level, university level, is there anything that the university could do to to promote more like use inspired science? Oh my gosh, yes, that's a great

[48:07] being open for businessquestion. I definitely think we could do right. So Ben Holton, the Dean of towels, he said this, he said this really well in a meeting a couple of days ago. He says Cornell has got to be open for business and what this means. And if you think about it, right, it strikes me that, yeah, we're we're a little bit like a developing country right now. What we want to do, you know, if you think about it, developing countries are just overburdened with regulation. Everything's regulated. You know, to get yourself to get a company or country ready for business, you've got to remove friction in the system. So coming back to my point earlier about how in the sort of probably in the 1970s people realized, you know, we, we don't want another DDT, right? And they they. You know, when, when recombinant DNA technology was invented in the 70s, loads of regulation was put around it. And over probably over the decades that followed, universities probably accreted, you know, just just as as a natural result of, I think I'm no expert on this, but I suspect as a result of that partnership between the, the federal government and the universities, they became increasingly risk averse and. And so as a. Result, you know, we put in all these regulations and regulation sort of becomes like scar tissue after time, right? And it becomes. I think if you think about if you, if you have scars, you know, and your muscles, it gets very difficult to move them. And that's the situation we're in right now. And so we've got to what we've got to do is we've got to remove that. And that means we have to look at. We have to look at how we. Do say material transfer agreements, we have to look at how we do filing of intellectual property, how we do licensing of intellectual property, how we, how we do conflict of interest expense reporting, how we how we account for travel. Do we even bother doing these things? But yeah, the university has to be open for business. They aren't right now. Do they need to be? So it's open for business. As a more corporations would come licensed technology and more service would come out of the universities. Is that like what the output would look like or? Yeah. It, well, it would be, it would be a sort of a more, I would say a more just a more dynamic university. So yeah, I think the university of the future would probably be generating conflicts of interest left, right and center, honestly and. I think the response. Of the university should be to say, OK, yes, we're generating conflicts of interest that means we're doing something interesting, which we should say we should embrace that we should say let's let's just do something interesting. Let's make new technologies let's get them out into the real world and and they they this is not to say that the universe this should be the universities pure focus, right. If you think about what what a university means is it especially in American University, right? It, it does a it does a range of activities, right. You know, it does it does sort of basic it does very curiosity driven basic science stuff that you would stuff that might take hundreds of years to come to actually show up in a technology. It does it does sort of like social commentary, right Does it does social activism. But I think, I think I do think that in amongst all that there has room has to be made for making technologies and and if you think about it, the the sort of the fundamental compact between the universities and the government. Starting 80 years. Ago was we are going to make new technologies that are going to make the public's life better, and I think we need to do a better job of that and precisely how we do that. I think if I could tell you an exact prescription, somebody would have done it already. So we have to experiment. We have to experiment with how we fund the science, how we evaluate it, how tolerant we are of letting people go for years, potentially without publishing anything. I think we have to try all these things. And if we do try a lot of things, I think some of it's going to stay. Yeah, that makes sense. So they're. Open for business as a general thing and then over time they'll solidify something more permanent. I agree totally and. Also, my, my feeling is, you know, society will change as well. You know, right now it, it, it feels to me that we're, you know, it feels to me that our society is stuck, but it also feels like we're on the cusp of coming on stock and, and maybe in the next few decades, we'll actually see an outpouring of new technologies. But then, you know, it might be that our, you know, our children and our grandchildren, they say, hey, wait a SEC. You know, these had some unintended consequences. You know, let's let's like, you know, let's put the brakes on this for a bit. And I think when the universities will have to change again, you know, they'll have, you know, they should be, they should always be responsive to, you know, the people in them, the society that they're in. You know, they, they should, they should be independent, but they should, they should sort of be listening to what people want out of them, I think, and what the people in them want out of them as well. Yeah, that makes sense. So. So, so, so buzz of for the closing question, I, I always ask the guests, what's the kindest thing that anyone's ever done for you? My gosh, that's a great. Question. I feel like I can think of so

[54:28] closing questionmany things actually. My gosh, I'm not going to single out any one person in my answer to this, but but but. You know, for all the. Problems that our society faces. It has been and it remains an incredibly generous 1. And I can't think of, you know, I grew up in England and I moved to the United States. And both of those societies have been and are really great accelerators for people like me. And throughout my life now, I've been very lucky to, to have found people who have to have benefited from people who have, you know, put some faith in me and, you know, sort of pushed me along my way. And there are almost too many of those to single out anyone. I think think, I think I'm very lucky to live in the society that I do live in. I hope that answers the question. Yeah. That's beautiful. Yeah. Thanks so much for sharing, Buzz.