Venki Ramakrishnan (Molecular biologist, Nobel Prize): “The experimental part [of drug discovery] is always going to be the bottleneck.”
Recent headlines about using AI to speed up drug discovery made me curious about what that looks like and where it is today. So I flew to the UK to interview Venki Ramakrishnan who is on the scientific advisory board of Demis Hassabis’ Isomorphic Labs.
He has described himself as a “failed physicist” starting originally with a physics PhD who changed fields because he felt his work was incremental. After pivoting into molecular biology without a degree he discovered the field of work that eventually led to his Nobel prize.
So aside from drug discovery, I also asked him about how AI is impacting the field of biology, how biology compares to physics, and the politics behind the Nobel prize.
I shot this episode myself as usual and I think it’s probably the best one I’ve done from a videography perspective. I found a nice room with good lighting and it is in focus this time. Hope you enjoy the episode!
Check out the episode wherever you get your podcasts: YouTube, Spotify, Apple Podcasts.
Timestamps
00:43 - How drugs are designed
04:54 - Why drug testing remains difficult
07:02 - How AI will impact the field of biology
10:35 - Switching from physics to biology
15:00 - How to choose research problems that matter
23:19 - Did lacking a credential hurt his career
33:21 - Why physicists succeed in other fields
35:10 - The politics of the Nobel Prize
38:37 - Top scientific book recommendations
40:05 - Advice for young people
Transcript
00:43 — How drugs are designed
Ryan:
[00:43] what is the actual shape of the work in discovering or designing a drug or maybe a molecule that binds to something that you care about?
Venki:
[00:56] The principle is that they’ve used AI successfully to predict how proteins fold, and that has worked really well. It’s not completely perfect, but even experimental work is prone to mistakes. So the question is, how do you go from there to understanding that you have a target molecule like a protein, and to stop it from working, you may have to bind a molecule in a critical pocket where it does its chemical reaction or where it binds something else.
[01:39] So essentially, you’re trying to block it from working. Occasionally, you might want to improve its function. That’s even harder. Blocking is the easier thing. And so the question is, can AI come up with an array of molecules? Traditionally, this has been done by some mixture of computational chemistry and just screening thousands of molecules, seeing if you have a hit, then seeing where it binds, then gradually improving it in an iterative process.
[02:12] But the question is whether AI can speed this up, whether you can have a better idea and so on. So I would say the early things look promising, but we need clinical trials. We need actual experimental proofs of principle that actually bring a drug out onto the market and show that AI has accelerated the process. Now, I think people in the field are optimistic, but I think you have to really wait for the results, I would say.
Ryan:
[02:47] When you think of that process of actually finding a molecule that blocks that critical pocket in the protein, what are the steps that you take to actually design a drug?
Venki:
[03:02] Well, okay, so AI can come up with a bunch of molecules that it thinks will fit based on recognizing patterns of interaction and so on that it’s been trained on, right? And then of those molecules, some of them may have toxic side effects. The question is whether AI can predict toxicity. In some cases it can, but I’m not sure it can do it in all cases. And then the molecules have to be able to synthesize them.
[03:36] Right. In an easy way, and then you have to test them. So the experimental part is always going to be the bottleneck, getting the experiments done, getting enough data to go to clinical trials, and then carrying out clinical trials. That’s always going to be the big stumbling block or bottleneck. And even in traditional drug design, many, many drugs fail in clinical trials, even though they’ve been very promising in animal studies or studies in the lab.
[04:15] And so I think it’ll become clearer in a few years how efficient and how much better it is. But I would say the people in the field are very optimistic.
Ryan:
[04:29] It sounds like AI could maybe help in the search phases or the brute force of actually— Yes, that’s the whole premise is that it can speed up and make that initial filter much more efficient.
Venki:
[04:35] So that’s the hope. And I think we have to wait a few years and see how it’s panning out.
04:54 — Why drug testing remains difficult
Ryan:
[04:54] But even if that was a perfect— let’s say it was an oracle, it could just give you something that binds. There’s still all these downstream steps in the physical world.
Venki:
[05:06] Oh yeah, definitely. Because I can tell you, even with things like monoclonal antibodies, which are very specific, there are people who went into critical care in phase 1 clinical trials because of some unexpected side effect, off-target binding. So you really have to do all the trials before you can release it on the market. So it’s not— AI could be very fast at its computational work, but the experimental work is still going to be the rate-limiting factor.
[05:45] Human biology is complicated. So it’s not—I don’t know if it’s possible to predict all of those potential side effects and the kinetics of the drug, how quickly the drug is excreted. These are all things you have to do experimentally at the moment. I mean, in some distant future, maybe we’ll reach a world where these things can be predicted, but I don’t think we’re there today.
Ryan:
[06:15] Is there enough slots for all the people who have drugs and want to do clinical testing?
Venki:
[06:22] Well, they have to fund it and find the patients and so on. So that’s the limiting factor. It’s not—I mean, the FDA, if you propose, if you have sufficient animal data and some animal safety data and a clear rationale, the FDA will say, okay, you can perform it. You can register a clinical trial, but you still have to fund the trial. Somebody has to fund the trial. Somebody has to find the patients.
[06:52] So it’s a big process. And big pharmaceutical companies are used to doing that sort of thing.
07:02 — How AI will impact the field of biology
Ryan:
[07:02] In other fields like math and computer science that are more closed, we see that these models are drastically changing the frontier and the state of the art. Do you expect the same down the road in molecular biology?
Venki:
[07:19] I think biology is intrinsically much more complex. It’s not a defined system like mathematics or computation. So my gut feeling is that AI has proven itself in some aspects of chemistry. For example, I talked about protein folding and AlphaFold, which won the Nobel Prize, but I think for complicated cellular biology, and especially at the organismal level, it is highly complex. It’ll be harder, I think, to make progress than with mathematics and so on.
[08:01] The other thing I notice is that AI has been, even in mathematics, AI has been very good at solving increasingly hard problems. But it’s not currently, as far as I can tell, and I’m not a mathematician, so you can take it for what it’s worth. I don’t see it as defining what is interesting, what are the big questions. Those problems were all defined by human beings. Okay. So will AI come to the stage where it says, okay, here are some really new things that we really need to understand.
[08:38] And by the way, here’s the solution. Okay. That’s a different kind of thing. And humans excel at having that forward vision. So if they’re going to use AI as a tool, sure, that’s great. But to expect AI to just do everything, it’s not clear. I think the best way to think of it is it could be an incredibly powerful tool for humans to use to solve complicated problems.
Ryan:
[09:14] I know in those fields, because the ability to propose a paper, the cost has gone down because of AI. I don’t know if you or your peers have noticed in biology or similar fields, is there an influx of papers, maybe AI-assisted, in either just the prose or maybe the experimentation?
Venki:
[09:35] I don’t know, because if it happens, it would happen a lot in computational biology and areas like that. Certainly, it’s made coding a lot easier. That’s accelerating science. And we talked about protein prediction. There’s now a new program released by DeepMind, which tries to predict what genes will do if mutated and so on. So I think things are progressing. And yes, it’s definitely accelerating biology.
[10:10] I think the more complex biology you get, the less impact it’s had so far, except for highly computational problems. But I think that could change. You can think of me, I’m not somebody who’s sort of this wildly optimistic type. I take a more cautious look at things.
10:35 — Switching from physics to biology
Ryan:
[10:35] You got a PhD in physics, and then at some point you did a hard pivot into biology. And I think a lot of people, whether because of sunk cost or some other reason, they might not have the confidence to pivot so hard. What gave you the confidence to switch?
Venki:
[10:55] Oh, I don’t know if it was confidence. There’s both a push and a pull there. I just wasn’t feeling very motivated about continuing my physics career. I thought the problems I was working on were not that interesting. And I didn’t see, with my particular graduate training and PhD, I didn’t see a real future for me in physics, to be honest. I thought if I stayed in physics, I’d probably end up in some second-rate or even third-rate position doing very incremental or boring stuff at all, if at all.
[11:41] And I thought that I was giving myself a second chance. So it’s not like I had this great confidence in saying, oh, I’m going to go off and do this other great thing. I just thought of it as, I mean, it’s like punting in football. I just thought, okay, I’ll give myself a second chance.
Ryan:
[12:02] When you were in physics, you had this, I guess, research taste, or the sense that continuing that research, those problems were not interesting, or they were not— Yeah, they wouldn’t go anywhere.
Venki:
[12:16] My thesis has maybe 20 citations after 50 years or something, so you can see probably nobody read it. And the thing is, it had almost no impact. And the thing is that biology, when I made the switch, was really booming. All sorts of things were happening. It was like going through a revolution. And I thought, oh, this is where the action is. So that was the pull. The push was that I wasn’t so thrilled about what I was doing, but the pull was that biology was going through a very interesting time.
[12:58] And it’s weird because that revolution hasn’t stopped. New things keep happening in biology that has really made it a very exciting place because as new tools appear, you can crack aspects of very difficult problems that you couldn’t before. You can get to the next level in difficult problems. So it turned out in hindsight to have been a good choice. And that was completely by accident.
[13:27] I read an article in Scientific American when I was a grad student in La Jolla, and the article was written by these two professors at Yale, Peter Moore and Don Engelman. And it was about the ribosome, which is this large machine that reads our genetic information, which basically resides on mRNA, which is a copy of DNA of the gene on DNA, and uses that information to make proteins.
[13:57] So it’s a very, very central molecule in the cell. It’s one of the oldest molecules of life, probably predates DNA because before the ribosome, the cell wasn’t making proteins in any systematic way. So why would it need genes to encode proteins? So it’s an incredibly ancient molecule that’s still absolutely central to life. And by that time, I knew what a ribosome was because I’d gone to this graduate school after my PhD.
[14:29] As you pointed out, I pivoted. But in the pivot, I started graduate school all over again. In fact, the first year I even took undergrad courses because I didn’t really know anything. And so I knew what a ribosome was, so I wrote to them and they offered me a fellowship to go to Yale. And that was the start of my sort of ribosome career in 1978. And that lasted my whole life, actually.
[15:00] Yeah.
15:00 — How to choose research problems that matter
Ryan:
[15:00] Earlier you were saying that even if AI accelerates the problem solving, the picking what problems are interesting, picking what problems are important, that at least today is uniquely human and valuable. Do you have any thoughts on how to pick interesting scientific problems to solve, and how do you pick?
Venki:
[15:23] Well, there are big problems like the origin of life or how does the body develop from a single cell into a complicated animal, complicated body? Or what happens to the brain and how does the brain work? How does it even make decisions? What’s the basis of your feeling of sentience? Things like that. So those are big, complicated questions. But you can’t answer them overnight.
[16:00] You have to say, okay, that’s a big question. Where do I start? And you have to sort of carve out a path that gets you closer to what you want to do or what you want to answer. And I think that’s where the judgment comes in. You have to combine something that’s important with something that’s feasible. You can work on something important, but it’s completely premature. The tools aren’t there. Even the conceptual framework isn’t there. You’re just wasting your time, right?
[16:33] On the other hand, if you just do some little incremental thing, you’re just wandering around and not getting toward some larger goal. So you have to somehow combine the two. You have to have an overarching vision, and then you have to break it up into steps that are getting you closer. So I like to think of it as, in physics, there’s a random walk and there’s also a directed random walk.
[16:58] Directed random walk means that you have a bias to get towards someplace. So it’ll still be a bit random. You won’t go there in a straight line. You’ll make mistakes, you’ll take detours and so on, but you’re gradually getting towards the goal. In a completely random walk, you’re just wandering around and you’re not getting towards anything. So I think that’s the difference between having a long-term goal or vision.
[17:24] What is the question you want to answer?
Ryan:
[17:26] I see. If I recall correctly, at the time when you started deeply getting involved in ribosomes, that space was not as booming?
Venki:
[17:38] Oh, it had gone through a boom in the ‘50s and ‘60s when people had discovered the ribosome. They found out what it did. They found out who the players were. They discovered mRNA. They discovered tRNAs and how all these things come together on the ribosome and make protein. And then the people who did that, I mean, some very famous biologists like Francis Crick and Sydney Brenner, they just sort of said, okay, the rest of the stuff is all details and we’re going to move on and look at development or the brain or something.
[18:15] But then there were a few people who still said, hey, wait a minute, this is a big, enormous molecule, half a million atoms, and it does these things, but we have no idea what it looks like or how it does it. So if you’re interested in that, in the actual mechanisms, then it was still an interesting problem. If you just were interested conceptually, that, oh, ribosome binds mRNA, joins, brings in tRNAs, joins amino acids together to make a protein, then the problem was solved.
[18:45] And you know, you can move on. So it’s a slightly philosophical difference. And the problem was to get to that next level seemed almost impossible in the ‘60s and ‘70s, which is partly why these guys just left. They sort of declared victory and left. And there were only a few people kind of banging away, trying to get little bits of information and so on. So when I entered the field, it was not that fashionable.
[19:12] And certainly by the time I finished my fellowship, it was really unfashionable. I had a very hard time getting a job. And then technology improved, and so on, and methods improved, and people realized it might be able to solve the whole thing at atomic resolution. And that would be a big deal. And so then it took off again. And now the field has drifted to more complex questions like, how are ribosomes assembled in the cell?
[19:47] That’s not a random process. It’s a very orderly process and highly efficient. And how are ribosomes regulated? How do you turn off— first of all, how is the production of ribosomes regulated? But then also, how does the ribosome— Yeah. How does the cell decide, oh, I want to translate this piece of RNA very efficiently and not so efficiently in other cases? How do I look at protein quality control?
[20:23] Is the ribosome product really actually good, or is it defective? And what do I do about it? So there are all sorts of regulatory questions, like if the ribosome stalls, the cell has to make a decision. Do I just now disintegrate this whole complex and start over, or do I relieve the stall somehow? And then viruses can hijack the ribosome to make its own proteins. So how does that work, and how can you maybe prevent that?
[20:54] So lots of higher-level questions beyond the basic structure.
Ryan:
[21:00] So when you were picking that unfashionable field, did you have a sense that the technology was advancing enough so that you could solve it, or was that just pure happenstance?
Venki:
[21:11] We sort of went in stages. First, we figured out where the components of the ribosome were roughly in space, but that doesn’t tell you a lot about how it works. And then we thought, okay, the technology’s there to take each little piece of the ribosome and look at its structure. But without knowing the context, that also in the end didn’t tell us much. And by that time, by the time we had done a bit of that work, 10 years had gone by.
[21:38] And then, really, after a sabbatical here in Cambridge, and when I went back to the US, I was at Brookhaven National Lab on Long Island, and then I went to the University of Utah. And at that point, I realized that maybe the time is ripe to tackle the whole thing. And there were other people. There was Ada Yonath, who died just this year, just a couple of months ago. She had obtained, along with Heinz-Günter Wittmann, the first crystals of the ribosome.
[22:13] But the field had been going on for 15 years by that time, and no structures had come out. And so a number of us felt you could maybe start having, go into it with some new ideas and new angles.
23:19 — Did lacking a credential hurt his career
Ryan:
[23:19] In your career, you had the PhD in physics, and then you pivoted to biology, and you didn’t finish a biology PhD.
Venki:
[23:42] No, because I went to do this fellowship.
Ryan:
[23:44] But you had the expertise for biology, but not the social signaling that, hey, I have a PhD. And I was curious, did that set you back in any way?
Venki:
[23:57] It might have. For example, if I’d gone and finished a PhD from UCSD in biology, maybe my CV would’ve looked a little better. But as it was, I had a physics degree in theoretical condensed matter physics, which no biologist could even understand the title of the thesis, from Ohio University, which is a good university, but not, I would say, like a top tier in molecular biology. And so I had this weird CV.
[24:32] So when I started applying for jobs after a postdoc, most people said, well, this is a rather strange CV, and probably put it in pile B. And I didn’t get any interest at all. So in the end, I went to Oak Ridge National Lab for a year, but then they had promised me a biology lab of my own, but then funding for that was not forthcoming. And so I left after 15 months to go to Brookhaven National Lab.
[25:04] And that’s where I got my start as an independent scientist. And that’s when I went on sabbatical to learn crystallography, which is the technique my lab used to solve the ribosome.
Ryan:
[25:18] So if you were advising a young person and they’re thinking about finishing that credential for the sake of whatever downstream benefits and social signaling, or—
Venki:
[25:30] It’s a mixed bag because maybe if I’d finished my PhD, I would not have gone into the work on ribosomes and my career would’ve been very different. It’s very hard to predict whether it would’ve been as successful or not. It might’ve been the safer option, but it’s not clear it would’ve been the better option. You can’t really predict. I would say to people, you have to do something that you really care about and that you think is interesting.
[26:07] And yes, you need good credentials. You should try to go to the best environment. And best environment doesn’t mean the school that’s highest ranked in some U.S. News & World Report or something. It’s the best environment for what you want to do. Okay. Are the people there? Are the mentors there really good at what they’re doing? Are they going to mentor you well? Are your colleagues going to be good?
[26:33] Are they going to be stimulating? Do they have the infrastructure that you need to get top-level science done? So those are the things you should look out for. And there are lots of places like that. And they’ll vary depending on what I thought it
26:50 — Physics vs biology
Ryan:
[26:50] might be interesting since you deeply studied physics and biology to ask you, what do you think the main differences are between the subjects aside from the obvious subject matter?
Venki:
[27:03] Well, biology is very complex. So a lot of questions in biology are settled by experiment. It’s very hard to predict theoretically what’ll happen. Although, as we discussed, with AI and computational methods, people are trying to do more prediction computationally. But it is a highly complex system. And in the end, you need experiments to settle what’s going on. And I would say, because it’s so complex, if you want to study the effect of something, how do you know that whatever changes you see are because of whatever you did, or it’s not just some random thing?
[27:54] So in biology, you always have to do control experiments. You add your factor, see what happens, and then you see what happens if you don’t add the factor. So you have to carefully design control experiments. And of course, in medicine, you have — this is why you have randomized clinical trials, which have proper controls. That’s an even more complex system, like a human being, because we’re all highly variable and so on.
[28:21] And so, but in physics, you can construct an experiment that’s extremely simple where the answer, from the result, you know exactly what’s happening. So physicists often don’t think about control experiments. It’s not part of their culture. They’re more about defining the experiment so it’s very sort of clean. And so that’s a fundamental difference. The other thing is physicists often will want to go into biology and want to predict everything from first principles.
[29:01] And you can’t do that. Every system has its own scale of complexity. So just because you can solve the Schrödinger equation for a simple system doesn’t mean you can then start applying it to understand memory, like the brain or something, even though they’re all governed by the laws of quantum mechanics ultimately. But it doesn’t matter because you are studying it at a completely different level of complexity.
[29:30] So you have to deal with it on those terms. And so that’s a problem sometimes that physicists have when they move into biology. They stop thinking—they never stop thinking like physicists. And what they need to do is stop thinking—they can use their physics training, but they need to start thinking like biologists and ask, what is the question? How do I approach this? And so on. And some people have been better at it than others.
Ryan:
[30:03] In a Q&A somewhere, someone asked you why you got interested in physics, and you replied that when you were young, physics and math were logical and pure in a sense, and biology was more memorization.
Venki:
[30:18] Oh yeah. The way it was taught, especially in India where I grew up, it was all rote memorization. And I never got a sense of biology as a kind of interesting detective puzzle. And I didn’t get that until much later.
Ryan:
[30:35] Yeah. Why is that? When I went to high school as well, it was similar. There was maybe a tier list of math and physics are kind of the pure ones at the top, and then maybe chemistry, and then biology is even more memorization. Is that in the nature of the subject or in the nature of how it’s taught?
Venki:
[30:53] I think it’s a little bit of both, in that biology has lots of complicated facts that you have to remember. And same with chemistry. You can learn about mechanisms, but you still have to remember a lot of stuff because otherwise you’re constantly looking up stuff. So I think it’s partly the nature of the field, but I think it could be taught a lot better in the sense of—and I think it is being taught better, much better than 50, 60 years ago when I was in high school.
[31:30] So I think it is being taught better, where you’re focusing on concepts and ideas and sort of why does this, apart from, of course, why is answered by evolution in biology. The answer to any why question is because evolution selected for that process. But the question is, how does this work? What is the sort of— what does it mean? What is the sort of purpose? Purpose, I don’t mean in some philosophical sense.
[32:05] We have no purpose except to exist and reproduce, I guess. Right. But the thing is, what is this pathway doing? So what is this enzyme doing in this pathway, for example? So I think there are ways to teach it conceptually that make it less of a memorization. In fact, it’ll make the memorization easier because you have some context for remembering these facts.
Ryan:
[32:34] Yeah, I guess some part of it is just the nature of the subject as well, because you could show up on a test not having deeply studied math, but you could figure out, derive things.
Venki:
[32:48] Up to a point. Yeah. Because when you’re sitting in a 3-hour exam, you can’t sort of reinvent all of mathematics on the fly, right? I mean, first of all, you’d have to be brilliant. And secondly, it would take too much time even if you were some sort of genius. So I think you do need to remember things even in mathematics and certainly also in physics. But I take your point. You can do more from first principles in those fields.
33:21 — Why physicists succeed in other fields
Ryan:
[33:21] So in the tech industry, there’s this pattern I’ve seen where physicists often do well in other areas like AI research.
Venki:
[33:33] Physicists have invaded almost every field. Yeah, that’s true.
Ryan:
[33:37] Why is that? You mentioned the physics training. What is it about?
Venki:
[33:40] I think because physicists are very comfortable with quantitative thinking. They’re used to numbers, they’re used to using mathematics, they’re used to using complex instrumentation if they’re experimentalists. So I think that gives them a little, I think it makes them well-trained for entering a number of other fields.
Ryan:
[34:07] In one of your lectures, it was about telling the story of how you won the Nobel Prize. You ended it by saying that science doesn’t depend on being a genius, but it depends on several other things. And one of the things that you said it depended on was skill. But when I think of a skilled researcher, I can’t help but think of a genius. So what is skill in research that is not intelligence?
Venki:
[34:36] Well, skill means that you’ve been very well trained in the art. You’re competent. You know what to do. You know how to carry out an experiment or a calculation. So I would say skill is different. I mean, genius means that you’re able to see things that are not obvious to the vast majority of people. You’re able to see a few steps beyond what’s obvious to the field. I think that would be my sort of definition.
35:10 — The politics of the Nobel Prize
Ryan:
[35:10] And in that same lecture, you talked about the politics of recognition, especially in the context of the Nobel Prize. And you mentioned these terms of pre-Nobelitis and post-Nobelitis, or basically when you’re getting close to the award but not quite having it, or you’ve already won. And I was curious, did you get pre-Nobelitis at any point?
Venki:
[35:36] I did. I mean, everybody did. I think what happens is that you do something important. The first thing you don’t think is, oh, I could get a Nobel Prize. That’s not what you think about. You think, wow, this is fantastic. But then you get invited to lots of talks, conferences, and so on. And everywhere you go, people say, hey, this could get a Nobel Prize. And then suddenly that kind of warps your own thinking.
[36:03] And then you start thinking, well, okay, it’s limited to 3 people and there are a whole bunch of people contributing to this field. And then I noticed that in conferences, people who are in this sort of pre-Nobelitis mode, they’ll very subtly talk up their work and they won’t mention other people’s work, especially competitors’ work as much and so on. It’s a kind of human psychology. And I just think that it’s a little unfortunate.
[36:43] And it’s partly the community’s fault and society’s fault that they give so much importance to this one award. I mean, there are lots of other prizes, the Lasker Prize and Breakthrough Prize. But if you walk down the street and, by the way, the Breakthrough Prize pays 3 or 4 times, 3 times a Nobel Prize. And if you share a Nobel Prize, it’s like, could be up to 9 times.
[37:09] Wow. Okay. So the thing is, if you walk down the street, you live in Manhattan, you walk down the street and you ask some random person, have you heard of the Nobel Prize? They’ll say, oh yeah, sure. And we say, have you heard of the Breakthrough Prize? They’ll say, no, what’s that? Okay. So you see, it’s had this because of its history and all these, it got launched at a time when genetics was being discovered, the nature of chemical bonding and reactions were being discovered, and quantum mechanics and relativity were being discovered.
[37:47] So all three fields had this once-in-centuries kind of revolution. And so the prizes went to these absolutely great scientists, like Einstein and people like that, Paul Dirac and Linus Pauling, people. So it was just, and Rutherford. So it created a kind of branding for the Nobel. And of course, the people who get it now, some of them might be in that class, but most of them are not.
[38:15] Okay, let’s face it. They’re not Einsteins or even Richard Feynman or something. So I think it’s created its own cachet. And so it’s not surprising that people who think they might have a chance really kind of ask whether they might get it.
38:37 — Top scientific book recommendations
Ryan:
[38:37] Is there a top book that impacted you, or maybe a book that you’d recommend to people?
Venki:
[38:44] In physics, I really enjoyed Feynman’s biographies, Surely You’re Joking, Mr. Feynman. And then he’s also had other short essay books, so I find him a very lively and entertaining writer. In biology, I was very influenced by a book that’s highly controversial, which is Jim Watson’s The Double Helix, because for the first time it made me realize that biology was not a rote collection of facts. It was like an exciting detective story to try and get at the structure of this molecule that contained the key to how life works and so on.
[39:25] Of course, it’s controversial because of his very frank description and also rather derogatory descriptions of Rosalind Franklin. But even with that, I know many women who have been highly influenced by that book. In fact, Jennifer Doudna, in her own autobiography, or memoir, talks about how she read it as a high school student and thought this was so exciting that she wanted to go into molecular biology.
[40:00] So I think it is, despite its faults, it’s a very exciting book.
40:05 — Advice for young people
Ryan:
[40:05] And then, last question for you is, if you could go back in time knowing everything you know now, what advice would you give yourself if you were just entering the industry?
Venki:
[40:17] It’s very hard to say because what seemed like mistakes at the time seemed to have worked out in some way. I mean, I went to Ohio University. I didn’t do so well. Partly it was my fault. I mean, I would say largely my fault. But then I met my wife there. So it was a life-changing experience for me. So I don’t see that anything has been really bad. I would say the advice I would give people is stay open-minded.
[40:54] And if things look like they’re not working, don’t be afraid to change. That fear of change is something that often will paralyze people. So they’ll stay in the same place. And I would say being open-minded and being open to new ideas, to new techniques, or even to new fields, or moving to new institutions. Change is sometimes necessary and can be quite invigorating. So my advice would be to stay open-minded.
[41:34] And not be too fixated on what you’re doing.
Ryan:
[41:39] Awesome. Well, thank you so much for your time.
Venki:
[41:42] You’re welcome.
