Eric Betzig (BS '83), Pioneer of Fluorescence Microscopy and Investigator of Cell Biology

In Eric Betzig's dream research scenario, he would occupy a world of small science: bench top experiments conducted by teams of two to three people. This was the standard practice until the twentieth century, when new technologies and new national and international priorities compelled massive collaborations. But as a visionary and a technologist, Betzig wishes he could access the research instruments that could be available centuries from now. As he quips in the discussions below, we know more about the composition of stars than we do human cells. It is an observation that perfectly encapsulates the duality of how much we know, and how little we know, all at once.

Born and raised in Ann Arbor, Betzig came to Caltech with a plan to go into physics, and his first significant exposure to biological problems came during his graduate studies at Cornell, where he developed optical microscopes that pushed the outer limits of resolution capacity. He speaks movingly about his time at Bell Labs, where he continued work on optical microscopes, and where he reveled amidst a research culture that was built for collaboration and discovery across the scientific disciplines. When the Bell Labs breakup compelled him to think about his next moves, Betzig decided to go back home to Ann Arbor. After initially leaving the workforce altogether, he joined the Ann Arbor Machine Company, and subsequently reconnected with Harald Hess, his old colleague from Bell Labs.

Their collaboration on photoactivated localization microscopy (PALM), which achieved new levels of resolution, is one of the all-time great stories in technology development. With minimal institutional support, it was a too-perfect distillation of Betzig's dream to combine the sociology of small science with the capabilities of futuristic technology. In 2014, Betzig was honored with the Nobel Prize in recognition of his contributions in advancing microscopy so that it can focus on cellular functions in their dynamic, living, state. It is the kind of enabling technology that will require decades before its significance is fully appreciated.

Today, Betzig is a professor at UC Berkeley, and despite the many titles and affiliations that capture the diversity of his interests and expertise, he insists that it's all just science. He credits Caltech for showing him the meaning of hard work, and that, above all else, is the fundamental characteristic when confronted by the all-consuming reality that we understand so very little of what actually happens inside a living cell.

DAVID ZIERLER: This is David Zierler, Director of the Caltech Heritage Project. It is Monday, March 4, 2024. It is my great pleasure to be here with Professor Eric Betzig. Eric, it is wonderful to be with you. Thank you so much for joining me today.

ERIC BETZIG: Sure, David. Thanks for having me. I didn't think I was important enough for an interview! [laughs]

ZIERLER: [laughs] To get started, please tell me your titles and institutional affiliations.

BETZIG: Oh, gosh.

ZIERLER: I pluralized that. I know you have more than one.

BETZIG: Yes. I am the Eugene Commins Presidential Chair of Physics at UC Berkeley. I am also a Professor of Molecular and Cell Biology at UC Berkeley. I also am a Senior Fellow at the Janelia Research Campus, which is in Virginia. That's where I used to do my work before I was here at Berkeley. Both at Janelia and at Berkeley, I am pretty much entirely supported as a Howard Hughes Medical Institute investigator, which is one of the best dodges you can get if you're in science. I highly recommend that anybody with a biological tilt keep that on their radar!

Science is Science

ZIERLER: We're going to unpack all of those titles and affiliations, but I want to start out with a really big question and deflate the idea that you're not important enough for me to speak to. I think this is going to get to all of things that you do in science and the way that you've been recognized, and I'm very curious to hear your answer. Your Nobel Prize was awarded in chemistry and yet what you do as a professor of physics is very important for optics, and what you're looking at is biological. What does that tell us about physics and chemistry and biology and about the sociology of award-giving in science? I wonder if you can reflect on all of that.

BETZIG: The first thing it says is that those names and boundaries are artificial, and that science is science. I would say that any advance I've had in my career, not just the Nobel one but anything else that has pushed me forward, has happened by getting out of my comfort zone and trying to take something from a field I know nothing about out of desperation, because the things I do know about are not adequate to get me to where I want to go. The sociology—yeah. We're skipping ahead in the story—or behind, depending on your chronological point of view—but one of the things I loved about Bell, and to a lesser extent but to some degree Janelia did this too, is that there was no siloization like is common in universities. At Bell you had Tony Tyson using newly developed cameras to study gravitational lensing and hence dark matter in the galaxy, right next door to David Tank who is figuring out how to use two-photon microscopy to look at neural activity in the brain, and duh-duh-duh-duh. When I was at Bell, every paper that I did was a different set of collaborators and they were all from different fields. I do really bemoan the siloization of universities and how they tend to work.

ZIERLER: I'll keep that siloization just in terms of how you think of yourself. By your training, by the way that you see the world, do you have a home discipline?

BETZIG: No. [laughs] I always feel like an outsider wherever I am. I think of myself as—I guess on the colloquial side, I'd say an inventor. On the academic side I'd call myself an engineering physicist. But I really feel like, again, any title is inadequate to describe—the fundamental thing that makes me tick outside of my family is just trying to push the needle a little bit in any field where I feel like I could make a contribution. If I feel like I could do that in sociology—not that I can, but if I felt like it, and I felt like I had an angle on it, I'd work on that. I just try to find out where my curiosity and where the needs are and try to find a way of filling unmet needs with my skillset or broaden my skillset as necessary, if I feel I'm close enough that I can get to the point where I can make an attack on a problem somebody else hasn't.

ZIERLER: Of all the things that you've focused on from all of the different vantage points, can you connect the dots in terms of what motivates the thing that you're trying to understand?

BETZIG: Again it's not so much understand but to make an impact. I don't necessarily have to feel like I came out of it smarter fundamentally or I made the world smarter about something, but something that improves people's condition, their lives. I'd like to believe that I earn my salary at all times. I want to make sure that I'm providing value for what I'm given. To whom more is given, more is expected, right?

ZIERLER: Let's go to those titles and affiliations now. Being named in honor of Eugene Commins, a great professor in Berkeley history, what does that mean for you and do you see any connection with what Commins worked on?

BETZIG: To his work? Not really, I'd have to say. He also mentored Steve Chu, and Steve Chu was at Bell Labs with me. He has basically followed a similar career of mine, with a bit of hopping, about ten years ahead of me. The one distinction is he became Secretary of Energy in 2008. While I have a deep and abiding interest in energy topics now, I'll never be Steve Chu in that regard. I never knew Commins, but I know Steve very well, and so I therefore am grateful to Commins to mentor a guy like Steve, who is teaching me new stuff all the time.

ZIERLER: The term "Presidential Chair," how rare an honor is that within the Cal system?

BETZIG: I have no idea. [laughs] You're again focusing on titles, and honest to God, titles are again just obfuscations, as far as I am concerned. You can have all sorts of distinguished professors who can't tie their shoelaces. I don't think in titles of anybody. One of the good things about getting a Nobel Prize—and there's a lot of bad things too—but one of the good things is you never have to feel like you're talking uphill to anybody. It also reveals again that people are people. It's not like these people who win Nobel Prizes are deities. It's the Shakespearean thing—some are born great, some achieve greatness, and some have greatness thrust upon them. I would say that of the laureates I've known, probably 80 percent fall in that latter camp. It's a question of being in the right place at the right time with a little bit of luck. Hard work too, but—and then there are the few elites, the Feynmans and the Heisenbergs and guys like that who really are made of different stuff. I think most people who succeed at a very high level, the one thing that I find somewhat in common among them is the willingness to just forge their own path. They're just not as drawn in by what other people think. They just follow their own path and let the chips fall where they may.

ZIERLER: If you'll humor me, there might be some aspects of the titles and affiliations that elicit a substantive response—it's Presidential Chair in Experimental Physics.

BETZIG: That's correct.

ZIERLER: Do you see yourself as an experimentalist? Is there any theory work that you do?

BETZIG: I have done a little bit of theory but it's certainly [laughs] not at the level of Feynman or Gell-Mann or anything like that. My one what I would consider theoretical contribution was—and we're kind of jumping around in the story—during my second round of unemployment as I was trying to think about what I wanted to do, I felt like I wanted to get back into science but I had been out of it for so long that I had forgotten everything. I actually started opening up my freshman and sophomore then junior year textbooks and homework assignments which I had saved all of that time. Relearning. I came up with what I thought was a pretty clever derivation and theory of new ways—or not new ways; nothing's new—but ways that you could interfere light to make patterns that would be useful for microscopy in biology.

At first you fumble around, fumble around, and then you start using some matrix formalism and so forth and you realize, hey, this is actually fairly cute! It's well put together. I have many, many papers that have been cited many, many times, and that paper, which is one of the ones I'm most proud of, has probably one of the least number [laughs] of citations. So, yes, I'm known as an experimentalist, and 99.5 percent of the time I'm an experimentalist. I get into theory things. We actually published a theory paper about a year—a pandemic paper. What can you do during the pandemic, right? I was looking at some optical type patterns I use in my work and trying to see if I could make them better. It's nothing more than sophomore E&M. Again, it's not the fact that it's understandable to a sophomore, but it's the fact that you sit and think deeply about something for a while and you realize, hey, maybe I can make this better.

ZIERLER: On the Berkeley campus, is it one professorship split between two departments, or do you have two professorships?

BETZIG: I'm 50/50, is what it's called. I'm half a head count, or FTE as they call it, in each department. The course that I teach is about microscopy and it's listed in both departments.

ZIERLER: How do you minimize the administrative burdens of double the faculty meetings and reports to the chairs and all of that?

BETZIG: I'm an asshole! I don't go!

ZIERLER: [laughs]

BETZIG: Again, I like to provide value for what I'm given. I have startup funds from Berkeley, but in five years I still haven't had to touch them because my Hughes money has been enough. My salary is paid by Hughes. My benefits are paid by Hughes. My research is paid by Hughes. As long as Hughes is footing the bills, I feel like I have an obligation to Hughes to do what needs to be done. As far as Cal goes, no, I would not come to Cal to do service and administration and teaching like my colleagues do because I think they're incredibly destructive to the creative process. I really feel like the whole Vannevar Bush endless frontier and what it has meant for the growth of academia has been a major mistake and has really limited the growth and impact of science. Cal is certainly high up in following that type of path.

ZIERLER: What you're saying is that one of Bush's unfortunate legacies is making administrators out of scientists?

BETZIG: Essentially that was the end result. I don't think that's what he was thinking of at the time, but yeah, the road to hell is paved with good intentions, and I think Bush is an example of that.

Continuing the Bell Labs Model

ZIERLER: What the Howard Hughes Medical Institute allows you to do bears some question, given how special it is. What is the significance? What does the Hughes Institute mean for you and for society?

BETZIG: Hughes follows essentially the same prescription that Bell did. Their motto is "People, not projects." You are not trying to get money like in a traditional sense in an academic institution, where there is a call for proposals on a particular topic, which enforces mediocrity, because again you're following somebody else's vision of what should be done. Often times, because of peer review you basically have to get along with your colleagues and do similar things to what your colleagues are doing, work as teams and write joint proposals, go to conferences where you don't piss off the other people who are going to be your peer reviewers on your grant proposals or your papers. It's all one big mass of mediocrity. Hughes is people, not projects. Again, they don't care how big your group is, how small your group is. They care about the science. They don't care where the science is published. They hire good advisors. You come up with your head on the chopping block every seven years and you have to justify what you've done. If you can justify it, they renew you. If not, they chop off your head. Then you'd have to become a real professor. [laughs] I hope that never happens to me! It's somewhat similar to Bell. Bell was the same thing. When I interviewed at Bell, the first thing they ask you—if they like you and they're thinking about you—is, "What would you do if we gave you an empty room?" That's what they care about. They care about the science, nothing else. No other metric matters!

ZIERLER: It begs the question, since it's all about Hughes for you, why Berkeley? You have to sit somewhere. Why Berkeley?

BETZIG: I wouldn't have come here in a million years except the fact that my wife was a graduate student at Berkeley, always loved Berkeley, wanted to come back to Berkeley. The number one thing in my life is my family, and so that's why I'm at Berkeley.

ZIERLER: Is there an institution of higher education that you would feel most comfortable given your predilections and your ideas about academia?

BETZIG: Not a standard academic teaching institution on Earth would I feel comfortable in.

ZIERLER: Including Caltech?

BETZIG: Including Caltech, yes.

ZIERLER: But you have to be somewhere, basically, to be a Hughes Investigator.

BETZIG: Yeah. We actually nosed around a little bit at Caltech at the time we were looking at Berkeley, but I kind of knew that the fix was in [laughs], so to speak, and that we would end up here. In fact, the day I married my wife I figured someday we'd end up at Berkeley. I knew this was the cost of being able to be with the person I loved.

ZIERLER: Is this true beyond the United States? Like if you were at a Max Planck, for example, would that work better?

BETZIG: I don't really have a lot of knowledge of what happens in MPI and other places; it's all based on output that I look at. But I think their group leader model where they have some really, really big groups is a really negative thing. I think the bigger your group is and the more you are disconnected from the science, the less productive things become. You just can't keep your hands on all the buttons on what's going on. I think in terms of incentives. Another Caltech alum, Charlie Munger, said, "Show me the incentives and I'll show you the outcome." That's really true. The incentives in academia are geared towards the system as it exists. You're rewarded for bringing in grant money. You're rewarded for mentoring lots of people. You're less rewarded for the quality of your science. Nobody even really evaluates the quality of your science except for some letters that you get when you go for tenure or whatever. There will be like ten letters that other people in the field will write.

Generally speaking, the vast majority of what you're judged on and how high you're going to get in salary and resources is based on teaching and service and things of that sort. These are not scientific outcomes. These are propagating the system. It's because it brings more money to the university. The more grants you get, the more overhead there is. The more students you mentor, the more tuition that is paid. It has been an exploding system. If you look at the cost of a four-year university today for a student, compared inflation adjusted to when I went to Caltech, it's insane! You look at administration in universities and how that has exploded compared to faculty or student, it's insane! The system is seriously broken. I just try to stay out of that system, because it's not a system that allows me to do what I've always wanted to do, which is to make an impact in science.

A Truly Solo Professorship

ZIERLER: Where do you put impact in terms of mentorship and interaction with students, which you get to do, which you have to do, as a professor? How important is it for you to have graduate students and to teach undergraduates?

BETZIG: I don't teach undergraduates, and I've never had a graduate student and I never want one.

ZIERLER: Wow.

BETZIG: There are many ways to have impact. It depends on your personal definition of what is impactful. I don't think replicating clones of myself is impactful. I don't think bringing people into my lab who have zero experience and then—so I'm supposed to sit and—the whole academic system is you start as a graduate student, you become a postdoc, you become very skilled at something by the time you're done with your postdoc. You then say, "Okay, I'm going to go to a university and continue this work." You go to the university and they shut you in a room and they say, "Write a bunch of grants! Get a bunch of people. Mentor these people." You have people who are inexperienced who are trying to learn what you used to be good at, and you're spending—every professor is the CEO of a small nonprofit. That's basically their role. They're not scientists! They're CEOs of small nonprofits. And their science is primarily an advertising system to be able to bring more money into the nonprofit. [laughs] Sorry! I just don't think the way other people think.

ZIERLER: Yet to state the obvious, you're a product of this system. You were a graduate student.

BETZIG: I'm a product of the system. Absolutely, that's right. Am I grateful for that? Yeah, I guess I'm grateful for that, but I think there are other ways to have had an education as good as I got at Caltech without having to have had it from guys who had gotten taken from their own labs in order to be able to teach me. There are ways of changing the system. Will the system change? No, because the incentives don't lean towards making a change. Until something breaks—and that will require again a deficit going so out of control they can't fight it anymore, or things of that sort, where they actually have to make a real adjustment—it won't change. I'm not trying to change the world. I'm just trying to find a path where I can do what I want to do, the way I want to do it, and the way I feel is most impactful for society. I think that me being in the lab coming up with new tools for biologists is a better use of my time and better for the scientific community than me mentoring some green graduate student or teaching an undergraduate class.

ZIERLER: Do you ever feel like you're missing out on the skillsets that graduate students and postdocs have? For example, I hear all the time that computation is so important these days, and younger people, they just grew up with these things in a way that senior professors do not. How do you balance those things?

BETZIG: At the graduate student level I don't think I would ever bite on somebody who had experience, but you bring up a good topic for me right now, because I feel like my career has always been about doing something until it fails and finding out how it breaks and when it breaks and why didn't it reach my dream of what I thought the impact could be, then thinking about that and either thinking about a fix or a pivot to something else. Right now I'm at one of those points because our microscopes now are really powerful, they create beautiful data, but they create data at four terabytes an hour. That's half a petabyte a week. We do not have scalable computational tools to extract the biological meaning and the discoveries that are locked within that data on hard drives. We developed all sorts of analytical solutions for this but they're not scalable.

The only real answer—and I'm the last guy to come to this field—is AI. I don't know squat about AI but I can tell you I'm spending [laughs] a lot of hours a day trying to learn about AI—what it's good for, what it's not, what are the difficulties. Because I feel like that's my next thing. Could I hire some graduate students to start doing that? Yeah, I could, but I think they'd be as green as I am, most of them. Most of them are not experts on AI. My preferred path is to find some experts who are at Google or Meta or places like that where the cutting edge of this is, and see if I can interest them in a problem which is, I believe, impactful for biology by doing so. If that doesn't work, I'll work my way down the food chain until I get to the point where I can find experienced people to do it, because I think that's a lot more effective. I have to find flexibly minded people. They're hard to find but they exist. Yeah, definitely not grad students. Postdocs, possibly, and I keep an eye out for a good AI postdoc or a good guy who is willing to dig into that problem.

ZIERLER: That is one asset being at Berkeley? You do take advantage of being in the Bay Area in terms of tech?

BETZIG: The question is, is it an advantage or not? The kind of collaboration that I'd like to do, it doesn't physically matter where we are. The advantage of the Bay Area is there are certainly a lot of people with a lot of AI experience. The disadvantage is most of them get paid way more than I can easily pay them. It's a two-edged sword.

ZIERLER: I want to go back to this question—it's a really fascinating one—of what the Howard Hughes Medical Institute allows you to do. Obviously this is an elite designation. The funding is not there to make this the norm across academia. What would you like to see in terms of the federal government, the way the NSF, the DOE fund science? How might that make things better?

BETZIG: Time and time again, NIH has tried to do stuff like that. They have something called the Pioneer Award. I applied for the Pioneer Award the same time I applied when Janelia was just being built, and it was a very similar process. It was just a five-page summary of what it is you'd like to do and then you send your CV in as well. It's not like an R01 with all these i's to dot and t's to cross about your previous support, blah-blah-blah-blah. Again it was just bringing some smart people into a room and making a decision about who to fund. That was fine, but again it doesn't have the staying power of Hughes because it's sort of a five-and-out kind of thing instead of a renewable thing. It's always trying to find the right balance of backing somebody who is good but giving them just enough fear that they know that—tenure is corrosive, completely corrosive—you want to have some degree of fear but you also want to have some degree of security. Finding that balance is always tough. Hughes does a pretty good job with these seven-year renewals. There are people who go into that room and they literally throw up, they're so nervous—and these are top professors from around the nation—because they know how important [laughs] it is to get it renewed!

ZIERLER: Is there anything like HHMI? Does it have any analogs whatsoever in science?

BETZIG: HHMI is probably the best one. Bell was even better. Part of the problem of Hughes is that there is a subset of people who take that Hughes money and it's just a means to make an even bigger group. They still get all their R01s and all the rest and so forth, and they still end up becoming fairly divorced from their own research, maybe even more so because they even have more money to throw around. Bell was heaven for me, because it didn't matter whether you had a Nobel Prize or were a new hire; the most people you could have in your group is yourself and one other, a postdoc or a technician. That was it. You get back to that question of collaboration and bringing interdisciplinary work—well, if you only have yourself and one other, the only way you're going to push things forward is by collaboration and interdisciplinary work with the guy down the hall! That was so powerful!

The one thing that I don't understand is that there has been many attempts to do something like Bell or Pioneer Award or—Max Planck has a similar model with their group leader positions. The only thing that was really stable for a long time was Bell. For about a 50-year period, Bell just had the same model. Every year you would be ranked 1 to N, like the NFL draft. There would be ten department heads and they'd go around—"Who's your number one? Who's your number two?" Ranked 1 to N. If you were in the bottom ten percent, you were told you shape up or ship out. At the opposite end, if you were at the high end, a lot of those people were at the high end because they created new fields, but now they were bumping up against the fact that they can only have one postdoc and one technician. They want to grow that field, and then they go to academia. That was a good model, because basically Bell was the feeder system to the top schools, particularly in condensed matter physics. Heck, a lot of those guys, even though they're 70 years old, still rule condensed matter physics. [laughs]

The Origins of Janelia Farms

ZIERLER: That's right. Eric, one last question on the titles and affiliations. Janelia Farms, were you part of its origin story?

BETZIG: Not exactly. The real origin was a guy named Gerry Rubin, who used to be at Cal. He was the guy who, with Chuck Shank, who used to be at Bell, put together at Cal the first completesequence of the fruit fly genome, the drosophila genome. That was the runner-up project to doing the Human Genome Project. So, he had some experience in doing a large effort. That was mainly done up the hill at Berkeley Lab. Everything I've been talking to you about, Gerry had come up with independently. His real motivation was the LMB, the Laboratory of Molecular Biology, where there was a revolution in molecular biology in the 1950s and 90 percent of it happened among about 30 people [laughs] at the LMB. It was very similar to Bell—exceptionally small groups, exceptionally small teams, really crummy resources. They were in this broken-down old building and so forth. They came up with the structure of DNA. They came up with how to sequence proteins, how to sequence genetic material, the whole central dogma of transcription, translation, and replication, all done by about 30 people over the course of about eight or nine years. Because they were all popped together in one tight little environment and that was it.

Gerry understood that model. He was Sydney Brenner's graduate student. He was supported by Hughes around 2000, and he pitched to Hughes the idea of creating something consciously modeled after the LMB and after Bell Labs That became Janelia. 2005 was just a crazily miraculous year for me. I was unemployed and deciding to get back into science, and I saw something in Physics Today where this crazy dude wanted to create a biological Bell Labs. This is just when I'm starting to want to get back. I said, "Holy mackerel!" I had been out of science for ten years, but I contacted several of my old contacts like Horst Störmer who was my department head at Bell. He won the Nobel in 1998 for fractional quantum Hall effect. I knew Chuck Shank who was involved with Gerry. I had them kind of make feelers for me. Then Gerry called up and said, "Do you want to come visit and we can talk?"

I went there and it was still a steel frame and a pit of mud, and we wore hardhats as we went around. At the beginning I let Gerry do a lot of talking, because he likes to talk even more than I do. He was a soulmate. Everything that I've been telling you in this conversation so far is exactly the conclusions that Gerry had come to. Furthermore, he said, "I am designing Janelia to be the anti-Berkeley." In terms of red tape, in terms of bureaucracy, he said, "No. Everybody who is hired on the administrative side knows it's their job to serve the scientists and as quickly as possible fulfill their needs so they can continue on with their work." I couldn't believe it. I couldn't believe—this will certainly come up in the story if we go long enough, but my best friend for many years named Harald Hess, he was my friend at Bell and so forth, and we built the microscope that won me the Nobel together in his living room. For years after Bell was gone, we just bemoaned the fact that there'd be nothing like this again. Why can't people see the right way to do science? And so forth and so on. I thought Harald was the only person on Earth who felt like I do. When Gerry came along, it was like, "Oh my god! I can't believe this. This guy—" Once I had an offer, the first thing I said is, "You've gotta get this Hess guy! He would be great." Sure enough, we got Harald, too.

ZIERLER: What does the affiliation at Janelia over the years do for you that's not possible with Berkeley, with HHMI, both technologically and in terms of generating good ideas?

BETZIG: In terms of good ideas, I'd say I've been somewhat influenced by the Janelia crowd. The two foci initially were neuroscience and tools, broadly speaking. The tools largely ended up becoming microscopes, in large measure by what Harald and I were able to accomplish. Idea wise, I still felt like I was trying to get ideas globally more than locally. Now, there were things I would try to do for my compatriots at Janelia and that did influence directions that I went into. Particularly for example I got into doing adaptive optics in microscopy because the problems on the neuroscience side when they were doing imaging were clearly obviously influenced by aberrations in tissue. I got into that for that reason. I now believe that it's one of the more important things I've done. Generally speaking, it was again Gerry's wisdom in making the organization he did. Originally, there you could have at most a group of six people. Again, there were lots of shared resources, which made this super effective because you didn't have to do your own cloning. You didn't have to do your own vivarium to grow animals. You didn't have to keep the computer cluster running. There was all sorts of staff to do all of that.

Six can go pretty far when you have those shared resources. But I didn't use it, in the sense that my group averaged three people every year for the—I was there from 2006 to 2018, 12 years. PALM, which we did before that, that got me the Nobel right before that, that was fine but I'm much prouder of many of the microscopes at Janelia. PALM was sort of the start of an explosion in biological imaging and biological microscopy. It's gigantic today. I know this is an asshole thing to say, but I truly believe that in those years that I was at Janelia up through 2018, we outcompeted the entire rest of the world with my group of three postdocs. I would say we lapped the world with my three postdocs.

ZIERLER: How do you quantify that?

BETZIG: It's difficult to quantify and obviously it's subjective based on my own arrogance, I guess, but in terms of what tools have made the most biological discoveries is the metric that I care about. By that metric I feel like—yeah. In fact, this revolution in microscopy that has happened over the last 20 years I don't think is a revolution at all. Certainly not compared to the quantum revolution of the 1920s or the nuclear energy revolution of the 1940s and 1950s, or the LMB revolution in molecular biology. Those were real scientific revolutions. But of the biological findings that you can take to the bank that have come out of advanced microscopes, an unreasonable proportion came out of my lab.

ZIERLER: Let's move on to some questions about Bell Labs. Joining Bell in the late 1980s—I've talked to Bell scientists who were there in the heyday, the golden years of the 1950s and 1960s. Do you feel like you got a taste of that era before the Judge Greene decision?

BETZIG: I got a little tiny crumb of that. Yes, because I was coming right as things were on that downslope. I'll tell you a funny story about that. Again, I went to Bell to continue the work I had done in graduate school, which was trying to do super-resolution microscopy by a different method than the one that won me a Nobel. The method that I was working on at the time is—shine light through a hole that's smaller than a wavelength. The light spreads really rapidly out of that hole, but if you put it close enough to the sample, you illuminate a subwavelength-sized dot. You can drive that around point by point. That was called near-field microscopy. I got in the door at Bell in order to do that.

I was working for the first year just building my lab, doing a lot of technology stuff. Everybody who goes to Bell in that era knows its history, and you feel like an ant around giants when you go into that building for the first time as a new employee. You feel like you're on probation. You feel like [laughs] how am I ever going to measure up to these people? A year in, another colleague—we were called members of technical staff—came to my lab to give me some advice. He said, "What you're doing is technology. Technology is fine but the only metric that really matters here is how many Physical Review Letter papers that you publish." That was Bell when I came.

That Bell started to exist I believe in the 1970s. That Bell did not exist in the 1940s and 1950s and even the 1960s, where again they were very much tied to practical problems. Guys like Shannon and others, they were really tied to problems of practical importance. Eventually this morphed, probably after Penzias and Wilson with seeing the signature of the Big Bang, into much more of an ivory tower, we have Nobel Prizes so we've got to therefore think deep thoughts, kind of thing. So, it was changing. I was kind of more in the mold of the old Bell. So, I have that datum. Okay, I've got to write PRLs. Well, I don't give a fuck about PRLs, okay? I'm going to do what I—I'm trying to make this microscope work because I think it can have impact. I came close to quitting because I was having so much trouble getting that microscope to do anything useful. I had some breakthroughs by year three. In fact, I told Horst in year two, "If I don't have a breakthrough in year three, you don't need to fire me because I'll quit." Then in year three I had these breakthroughs, started doing applications and so forth. Once a year—Arno Penzias was the VP at the time—he gave sort of a state of the union address in the auditorium about what Bell is doing. All of a sudden my work was the poster child for the sort of applied work we should all be aspiring to do. [laughs] That was probably 1992. Then in 1994 when I realized all the limitations of my near-field technique and I realized I had reached a law of physics dead end you can't get past, I was ready to quit.

Just as I'm going out the door, my best friend Harald, who also had his own breakthroughs in scanning tunneling microscopy at low temperature at Bell—by that time they had bought National Cash Register company. Now you had the financial types starting to control AT&T. Man, did they ruin that place! [laughs] They wanted everybody to think even more relevantly to the marketplace. Harald was having to spend half of his time to figure out how they could use spectroscopy to figure out which fruit was in the shopping cart, so they wouldn't need to put those little tags with the four digits on them but it would just automatically—you would just drive your shopping cart through with the fruit and vegetables and it would automatically—so it went from "Only Phys Rev Letters matter" in 1988 to "Let's figure out what fruit is in the shopping cart" in 1994. That was a rather big culture shock [laughs], I would say, to guys who were doing stuff for a long period of time. It changed very rapidly. I got a little taste of some of the old Bell, but it was such a steep change over the time that I was there.

ZIERLER: Culturally, sociologically, this was happening independent of the legal decision that broke up the monopoly?

BETZIG: Exactly. The legal decision to break up the monopoly was 1984. I joined in 1988. The budgets and everything really didn't have much of an impact until after I was gone. The budgets were still stable and everybody was still able to do what they wanted. Once the suits got involved, more involved, things really changed. NCR wasn't that big of a change, but in the dot-com bubble startup when all of the fiber laser companies and all of this stuff are starting to take off, that's when the suits really thought that they could try to make something profitable [laughs] out of what we did. To Bell Labs' everlasting shame, they did a horrible job of monetizing all of the discoveries they did there, a really horrible job. But did it help humanity? Optical communications and networking and just Unix and C++ and so many things that we take for granted today all came out of Bell Labs. All the stuff that makes our modern world came out of Bell Labs. Unfortunately Bell Labs didn't make a penny out of it [laughs] but it was certainly impactful. AT&T then split off Bell Labs as something called Lucent Technologies in the 1990s. Lucent became a high flyer in the dot-com bubble. Once Lucent crashed in 2000 or 2001—it coincided with the Hendrik Schön scandal—those two were the final two nails in the coffin. After that, there was a huge diaspora of people. Harald left in 1996, I think, under some frustration. It was a trickle starting from probably 1996, but it became a flood around 2000, and then there was nothing.

ZIERLER: To clarify, is this to say that when you joined Bell, this mythical idea that you never had to justify research for the company—

BETZIG: Well, you have to justify it.

ZIERLER: —no, no, for the company's bottom line, for profit reasons.

BETZIG: Right, right, yes.

ZIERLER: You never had to do that?

BETZIG: That was a bug and a feature at the same time. I thought even from the beginning that if I continued with—look, I'm an inventor. I like to do applied work. My degree at Caltech is Physics. My degree from Cornell, PhD, is Applied and Engineering Physics. I always wanted to do applied work. That's why I was working on that microscope. I had a religious conviction but no proof that it would be valuable to the bottom line in some way. In fact, at one point, one of the spinoffs that came out of it was—at one time we had by the far the world record of high-density data storage using near-field stuff. That started a spinoff and all of this other stuff. So, it had a chance of doing that. But again, if you're trying to monetize research, it's difficult to also find that happy medium between independence and commercial relevance. Organizations that have a broader mandate have a better ability to be able to think broadly about how much rope to give the people in the organization.

The classic example right now, and one that I'm incredibly jealous of, and if I were 30 years younger and more nimbly minded I would be there today, is SpaceX. Trying to make humanity multiplanetary is a pretty big goal that involves many, many, many facets beyond just how good of a Merlin engine you can make. How do you keep people alive in space for long periods of time? It's such an interdisciplinary problem that almost anything that you would come in there to do could have impact on that problem, particularly if it's in the back of your mind to do that. There are opportunities like that today. The more narrow the focus is of the company, you can dive deep into that one thing but you'll miss something that might actually be far more impactful that's outside of your blinders.

ZIERLER: I can't help but note that you said SpaceX and not JPL.

BETZIG: Oh, JPL has become dysfunctional. Are you kidding me? Like the Mars return landers proposal they put in? That's a joke! They clearly have a management problem at that place! It was awesome when I was there! When I was a sophomore I had an optics class in this auditorium in one of the EE buildings—I can't remember its name—and they had closed circuit monitors. Voyager was just going to Jupiter right then, so we were like the first on Earth to see the volcanoes on Io coming in live off of the feed there! Those Voyagers are still operating! [laughs] It's amazing! The stuff that JPL has done with Mars rovers and so forth, it has been great. JPL has had a very storied and righteously lustrous reputation. But man, they really fell off the wagon in the last decade. They need to clean that place up. One man's opinion. A space buff's opinion.

What Was Lost With the Bell Breakup

ZIERLER: A really broad question, the road not traveled—I'm sure you've thought about this—what was lost when Bell Labs broke up? What was lost scientifically? What was lost for American ingenuity and leadership?

BETZIG: It was probably the last best place for people who wanted to do science the way science was done pre-World War II. I give a talk about once a year—in fact I gave this to the Caltech Alumni in 2017 at the Alumni Day—about the historical connections between microscopy and astronomy. One of the take-home messages of that talk is that up until the twentieth century, almost every major advance in either of those fields was by individuals working alone, often not trained scientists—people who did winemaking, did carpentry, were involved in making drapes. Or like Herschel, he was a composer. It was just a burning passion for them. Many of them were doing it on their own dime, just as Harald and I did. Harald and I are the perfect example of that. I won a Nobel Prize for a microscope we built with $25,000 each of our own money on his living room floor. I feel like I'm the last example of that type of science.

A lot was lost. Bell allowed people to pursue deeply, think deeply about a topic, without distraction. When it was gone, it was the last bastion of that type of environment. Janelia was an effort to recapture that. Janelia, after about I'd say six or seven years, really fell apart. It really became much more academic in its mindset. Even though they didn't have to write grants, they started to think like academics, grow big groups, do a lot of really big collaborative efforts instead of individual thought. Invention ideas come out of the individual human mind. There can be input from others, but ultimately the spark of creativity ends up coming out of one individual's brain. The way that they get that is by total concentration on the problem. If you look at Feynman—if you read anything about his history, developing quantum electrodynamics—when he was at Cornell, he was so wrapped up in the—he was thinking about spinning plates and gyroscopic effects and stuff like that. He was so wrapped up in it at one point that he fell asleep in a pile of leaves! [laughs] There have been times in my life when I have been fortunate, particularly when I've been unemployed, to really be able to think deeply about a problem, and it's so essential to the creative process, because you exclude all the extraneous stuff. All your clock cycles are thinking about the problem. When they're not—if you're jogging or taking a shower—then your subconscious delivers the answer.

The basic idea that led to PALM wasn't when we did the PALM; it was ten years prior, after I left Bell. At Bell I worked 16 hours a day, seven days a week. When I left, I'm a house husband, and I'm pushing my daughter around in a stroller, and it just pops into my head how I could combine a single-molecule experiment I did with a low-temperature experiment I did with Harald to come up with a different way of doing super-resolution. Why? Because all that stuff was completely filling my cortex. The subconscious mind is where really the creativity comes from, but it needs to be starved of anything except the problem. Modern science does not allow individuals to think that deeply about a problem. There's too many distractions! If you talk about momentum, there's nothing that breaks mental momentum like having to do anything like teach a class or [laughs] do service or whatever. It has been incredibly corrosive and really in my opinion impeded the progress of science that we don't have opportunities for people to be able to do that.

From Technology to Curiosity

ZIERLER: Let's dive a little deeper into that, how you define a problem and the interplay between technology and discovery. Is your starting point always technological progress and seeing what comes out on the other side, or are you sometimes motivated by what we call curiosity-driven science and you need to engineer the technology to figure it out? How do you work through that?

BETZIG: I would say it is a 90/10 balance with the technology and then the curiosity driven. I'd like for anything that I do to feel like there is a beneficial impact to society. I'm not a Feynman but I don't think I could ever be a Feynman and be so far upstream of the eventual impact. In terms of trying to figure out quantum electrodynamics, he's not thinking about how this is going to change communications or anything else. Or Einstein with generally relativity, which is absolutely essential to be able to make the GPS network to work, he's not thinking GPS network, right? I wish I were that pure. [laughs] I am not. I am a guy who wants to say, "What's an unmet need and is there something I can do to meet that unmet need?" Usually for me, at my age—in the beginning that's a hard problem. It was again a hard problem like when I was unemployed the second time after leaving my dad's company.

If you're really thinking about application like I do most of the time, then when you're done with a project and you're trying to shift gears, that's when you have to do the exact opposite of everything I just said about focusing on a problem. You have to take the blinders off. This is a problem with most scientists again, is that they never really take their blinders off. They never really think about stuff outside—not even outside of their field, but outside of the tools they currently use to do what they're doing, the organization that they have in their group, and like that. To them, they're fish in water and they don't realize the water that they're swimming in. When I want to pivot or do something new, then it's really, really important to take the blinders off and be as agnostic as possible about the possibilities and start winnowing them down until finally you decide to make a bet and you put the blinders back on.

The other ten percent, though, is the curiosity. Particularly with microscopy, one of the fringe benefits of it is that the images are fucking beautiful. Life is incredibly beautiful. Life, particularly when you can see it live, is incredibly beautiful. The problem is that the vast majority of biology for the last 100 years has been by looking at dead stuff. Molecular biology, biochemistry, structural biology—they're all about zooming in and looking at dead stuff. You will never understand a complex dynamic system by just looking at its parts. You have to understand how those parts dynamically interact. Microscopy is a really good tool. It's the only tool we have. Optical microscopy is the only tool we have to be able to see at reasonable resolution the subcellular dynamics happening inside of cells. I become captivated by that, first because of its beauty but also because of its mystery. That other ten percent of me is trying to get a handle and an understanding of how you go from inanimate molecules to animate cells. That's the fundamental mystery [laughs] of biology as far as I'm concerned. To that extent, I consider myself a real scientist. To that extent, I feel like at one time we did have an impact, and that was by using PALM-like techniques of single-molecule tracking.

The biochemists have all sorts of—you open up any textbook and it's filled with models of things like transcription, and how RNA is produced from DNA, and so many things. All of this comes from like looking at Western blots or chromatography columns or things like this. They see that protein A interacts with protein B, but then it's just their imagination that is trying to figure out what is the actual picture, and what is the dynamics behind it? They had no clue! It's all just speculation. This whole model came up about transcription happens by all these different proteins that have to come together at the right site to recruit another protein, which is a polymerase, which then drives along the DNA and spits out RNA. That's the central dogma that has been around since those LMB times. By looking at those individual proteins that have to come together, by single-molecule techniques, we saw that they were only sticking at that site for a few seconds at a time, and there was no time in which they were all there. That whole model of how that happens was completely erroneous!

It makes sense because if you look on publicly popular science channels or something on YouTube, you'll see processes like transcription done as a molecular simulation. You'll see, for example, when you're trying to do transcription, this polymerase going along RNA, these nucleotides come in, and out spits a ribbon of RNA. It's like, by what magic are they hoovering in these [laughs] nucleotides to spit this out? That's not in your little pretty picture there, your pretty animation! Everything is stochastic! Everything that happens in the cell, everything that we are, is due to the stochastic motion of single molecules with basically Brownian motion which is then skewed and making a weighted Brownian motion based on the stickiness of the individual partners! That's it! That's the fundamental—Brownian motion is the powerhouse of the cell, not the mitochondrion.

We learned all of that from this and we realized the process was different. How would things still come together? It's based on the stickiness of the molecules. How are they modulated? They're modulated because there are parts of the protein that are intrinsically disordered that act like Brillo to get them together. If you knock those off, it doesn't happen. At the same time, X-ray crystallography and cryo-electron microscopy, which is the way biologists look at proteins, can't see those things because they can only look at ensembles. Those things aren't the same in every unit because they're disordered, so you can't see them! So, this live imaging was real important as an addendum to the central dogma of biology. That to me has probably been the biggest hit of my tools so far. It led us to do a startup company around it, to basically use those tools to look at the motions of proteins in cells and to look at changes in that that are due to disease, and to then figure out if you can find compounds that can modulate that and then recapitulate the normal state. So, yeah, there are times when the biology really gets to me. I've been fortunate to accidentally stumble into a love of that topic. But it's again, for me, still largely a frustration, because I think most of the biological world is missing the point [laughs] of what biology is doing and why it's important.

ZIERLER: As an inventor and a scientist, how do you think about developing technology that is enabling discovery for your own work and for others? When are you thinking about a technology because you're going to be the person to discover it, and when is it something that's too far afield and you just want to get this technology out there for others to use?

BETZIG: It's almost always the latter. It's not like I say, "I have a burning biological question and I want to make a microscope or a tool to be able to answer that question." I don't think it has ever once been that. It has always been, what are the limitations of current technology? Who are the customers? I always like to think for anything I do, who is the customer? What is the customer missing? If those happen to be biologists, fine, then they're the customer and I talk to the customer. I find out, "What is it you want?" For most of my career, that was super-resolution. Super-resolution you didn't have to think very long to think to yourself, if I could make a tool that can look at living cells with the resolution of an electron microscope, this will have some influence on biology. [laughs] You don't need to be a very strong biologist to have that conviction.

That's exactly where I was when I went to grad school and went to Bell. That was the goal—make an optical microscope with the resolution of an electron microscope. Then with near-field, that goal failed and I thought I was done, but then it turned out the various pieces came together to make that a lot more realistic goal ten years later, so then I dropped everything and Harald dropped everything and we did it. It worked, but it has its own limitations. If you're looking at single molecules, you're not looking at a lot, right? Every cell has ten billion molecules and you're looking at them a few at a time, and you're throwing light on the sample which can hurt it. What happened after PALM was this constant thing of, dammit, we bring people into the lab to use the tool, and it gets them either nowhere or a little bit and then we hit a wall, because the tool is limited, because it's damaging, it's too slow, it's whatever. Then the engineer in my head says, "Okay, maybe this isn't the right tool for them, but they're telling us that the customer needs something more. Let's put our thinking caps on."

Then that led to my lattice light-sheet microscope. I was writing the proofs for that paper when I was called by Stockholm when I was sitting at a table in Munich at the time. To this day, although it doesn't get anywhere near the attention that the super-resolution does, I still think it's going to reveal the most biology by far. Certainly in my lab it has revealed way more biology than super-resolution. But then it had problems, and its problems were that it's fine to look at cells on cover slips, but cells didn't evolve on cover slips. Biologists know that the phenotypes that you observe in a cell are the result of gene expression. Gene expression is due to regulatory networks that are influenced by the external environment. If you don't have the environment right, you're not going to have the phenotypes right. It doesn't matter how good your microscope is; you still won't see reality. Ultimately you need to see cells in the environment in which they evolved.

The problem is that the cells are heterogenous and they have different refractive index across them, so the light gets scrambled. Then it's like, oh, well, astronomers dealt with that; look at the damn Keck Telescopes! So, you put adaptive optics on it, and now you can look at the cells in their native environment. Then you say, "Okay, that's great" and we take lots of data—behind me here—broop!—lots of fun stuff—but it's still largely pretty pictures. Well, not pretty pictures; pretty movies. You can get some insight from those movies, but to quantify it and to gain deeper insight you have to quantitate it. Then we run into limitations of the data, which is now getting me shifting into the AI. So, after PALM, it has been finding what's good, banging your head against a wall, saying, "Okay, I'm an engineer, is there a fix?" Then, doing the next thing, banging your head against the wall—"Is there a fix?" Boom, boom, boom. That's kind of what has led me. It hasn't been really led by a specific scientific question but it has certainly been led by an understanding of what is limiting biologists, and having input from biologists as to what they would like to have, to go to the next step.

All Microscopy All the Time

ZIERLER: Some overall questions about microscopy and your research. First of all, is there anything you do that is not microscopy?

BETZIG: Not really. I'm at a crossroads again. When I came to Cal it was a bit of a crossroads, but now five years in I'm at a crossroads again. I don't know where I'm going to go at this point. This is a long answer. I've already told you that I feel like the only path forward for me now with what I'm doing—the best path forward is to marry advanced AI to our latest data. I may go that path. In fact, I'm starting to advocate for that path now. I've written a manifesto on it that I hope to publish. I hope to get funding. The problem is that a lot of the latest tools developed on AI in vision—like Google's Vision Transform and Meta's Segment Anything—they are a much simpler scale. Looking at 2D images is a lot simpler than looking at the 5D images that we have. It isn't quite clear how it scales. You can make guesstimates but they're really guesstimates. So, I really need to learn more about the feasibility of applying AI to my problem at the current state of the art. I am sure it will tax the state of the art even for the best organizations on Earth to do this.

That brings up the other part. The first part is, is it doable at all? The second part is, if it's doable, it's certainly not going to be cheap, and can I find an organization or organizations that would fund that and find enough good people who would be willing to work towards that goal? That also means that all of a sudden it becomes now a big thing. I've always done stuff myself with my own hands at the tabletop. That's what I enjoy doing. I have a Nobel Prize but I don't want to be some fucking old Nobel Prize guy, the titular head of some organization that's doing some big thing. I have a big bias against large organizations of any sort. So, I'm dealing with this question. I believe this is the path forward but I'm not sure that I want to do it, and I'm not sure I can convince anybody else to take it as seriously as I want to do it. The problem with big organizations is Price's Law. Do you know Price's Law at all?

ZIERLER: Sure.

BETZIG: For the audience, it's basically that half of the output of an organization is done by the square root of the number of people. As your organization gets big, your output gets small. Why did my three people plus me outlap the world? Because the square root of four is still a pretty good number. But you take groups elsewhere that have 50—and when they start working collectively together under shared incentives, then you can call it thousands working together—and it just—pshh. Price's Law is one of the basic problems of academic science in the Vannevar Bush era. I'd like to push it forward. It's super frustrating to have such fantastic data and not be able to get the information out of it. It just frustrates the hell out of me. But I'm not sure I want to put the skin in the game at the degree I would want, and I'm not sure I could develop an organization that even if the technological tools exist could still succeed because of these human factors. Anyway, there's that. That's one option. These are the kind of things I think about in my head all the time.

The other one is about a year ago, I read a book by Vaclav Smil. He's a professor in Manitoba who for years has been studying the energy economy—how energy is produced, how energy is consumed. What do we now? What can we do in the future for energy? It's one of those few books that kind of changed my life, I'd have to say, in the sense that I really understand the importance of figuring out better energy solutions in the twenty-first century. The U.S. won't be so bad off because we are blessed with a wealth of energy sources, but much of the developing world—there are a billion people on Earth who use as much energy per day as your refrigerator does. There's a huge correlation between energy use and life expectancy, standard of living, infant mortality, any other measure you care to make. On the other hand you have climate change. The entire developed world could stop growing altogether—which I don't think is a good thing but even if we did—energy use and CO2 output will continue to increase as the developing world continues to develop. I don't think we have a moral right to tell them to not develop, to continue to have their children die young, to die themselves in their fifties, to live lives where they're burning dung for fuel. I don't think that, because of climate change, that this is a moral thing. We will produce more carbon as a result, and so we have to come up with better energy solutions for those reasons. Plus we'll start to run out of certain sources.

I dove for a while deep into the solar and wind thing, and I've sort of come to the conclusion that they are not good solutions. They are good solutions at small scale, at distributable—I have solar on my house. It's great. I drive an electric car. But I don't drive an electric car for climate, because when you look from the manufacturing end of making the battery and everything all through to the end, it's about a wash with an internal combustion engine. There's really no net gain. Solar ends up being largely a negative by the time you're done if you assume a 25-year lifetime. It's intermittent, and that's the other big problem. The intermittency of wind and solar is just death to an electrical grid. You need nuclear or fossil fuels to take up the—the poster child for this is Germany. Their renewables is now at 40 percent. They get into trouble every winter because the Sun doesn't shine and the wind doesn't blow, and so then they start burning a lot of coal and import a lot of electricity from France's nuclear reactors.

To make a long story short, I have no idea how I can contribute to the energy problem, but I realize that it is probably the defining problem of this century and I'd like to contribute. At the very least, I'd like to be able to spend more clock cycles thinking about it. Again, I'm in a good position where how I spend my time is largely defined by me, but there's an opportunity cost for any particular choice of topic. The third one of course is space. I've been a space buff my entire life. I went to Caltech specifically to get training so I could become an astronaut. I grew up with Apollo. I knew the name of every astronaut. I could tell you today that Gus Grissom and John Young were on Gemini III. By the time that I graduated, the shuttle was about ready to fly. I knew before the first flight that this was the biggest mistake to go down the route of that vehicle. It was a major mistake. And it was proved to be a major mistake. So, being an astronaut was not for me.

SpaceX is changing that equation. I have my fingers crossed under the dim hope that it's a race between the entropy taking over my body versus the cost of spaceflight coming down if Starship gets to be routinely in operation, that maybe I could afford a ticket to at least go to low Earth orbit before I'm dead. If I could get a one-way ticket to Mars, hell yes I'd take it! The right people to send to Mars are old people! Because we don't have as much to lose when we die [laughs]. That's a quixotic dream. It wouldn't be necessarily a career, but I am so jealous whenever I look at SpaceX do a big launch and you see their mission control and all the people there and like that. Those people are living the dream. They're motivated and doing great things. Again, I can't run a large organization but I can certainly appreciate people who can put together a large organization that works that effectively.

AI For Small Science

ZIERLER: At this juncture, your obvious commitment to small science, is advanced AI the way for you to continue doing foundational work without needing a ton of people around you?

BETZIG: If I could get it off the shelf now and it would work for my problem, that would be great, yes. I don't think it's in that state. AI still has a long way of development go to be able to tackle the problems that I want to do with their—it's far beyond in complexity what the vision transformers and foundation models that they have right now are. Obviously it's moving quickly. It might be another case of maybe what I should do is let it lie fallow, just like I did for super-resolution for a decade. Then a decade later, it was ripe and ready to go. It might be that way with the level of AI that we want to have. Between new algorithms and of course better hardware—every six months Nvidia comes out with something that is three times faster [laughs] than the last generation. Sometimes it can be too early. There's a lot of cases of good scientists, inventors who attack a problem but it's just not time yet. The pieces just aren't in place. I have a feeling for AI with my problems the pieces are not today in place. I can help try to push it forward to get those pieces in place. The other alternative is to work on energy or something, and hope those pieces fall in place in the next decade and keep an eye on it.

ZIERLER: In terms of where AI is now as a research tool, you're dealing in petabytes of data. You're obviously drowning in data. There's more data than brains to assess it all. Are you thinking of AI essentially as the best tool to find the signals amid the noise—

BETZIG: Yes.

ZIERLER: —or are you talking about AI doing something beyond that?

BETZIG: No, I would be happy to have an AI that can essentially do all the things that we humans could do to extract meaning from that data but to do it at scale. We have done this type of stuff with analytical tools. The first paper we had on using my lattice light-sheet with adaptive optics, we showed some analysis of some of the data. Obviously only a small fraction, but it was one very skilled programmer who is also a great biologist working three million CPU hours with one year of his time writing custom scripts to basically see 10-5 of the insights that's buried in that data. We need the AI for scalability. We know what we want to look at, or we think what we know what we want to look at, as a start. I'm sure once we get answers from what we want to look at, there will be many, many, many other questions that we would pose to an AI. But the AI doesn't ever think for us. There's still some kind of cost function that you're optimizing. The human brains still determine what that cost function is.

ZIERLER: What are the signals that you're concerned we're missing right now that AI would elucidate?

BETZIG: I made the argument when we were talking about the biology that the correct way to study cells is to study them in the whole organs. Again with the lattice adaptive optics, we can do that, but the very first step is very different to do analytically, which is just to segment the cells in the tissue. It's very basic. You have to know where one cell begins and another one ends before you start quantifying what is happening inside of single cells. Again the boundaries are there. The cells are really perverse in their morphologies. Think about the craziest—all these little spidery little protrusions and all this. That's the reality of cells and tissue. Having analytical tools so that happens, so you can do that segmentation. But man, segmentation is exactly what Meta was able to show with their Segment Anything, but they're doing it in 2D. It's really good. Their accuracy is stunning. But it's not at the scale we need.

The very first step for an AI is to be able to segment our data. Because if you see the tissue all together with all the organelles in it, it's a hash! You can't tell anything! You can't divine anything out of that. You have to be able to take these pieces apart, but at the same time while you're taking them apart the AI is also trying to understand the correlations, long-term relationships, long-distance relationships that happen between cells and tissue. There are many, many levels of this, with the segmentation just being the ante into the poker game. From there you try to figure out how organelles interact. You try to figure out, what are the different cell types in different parts of the tissue? Do they change over time? What is the state of different cells at different times? Where are they in their mitotic cycle? What is happening in terms of the organelles? Do the mitochondria ever contact the endoplasmic reticulum, and is this a functional contact? Then, what's its function? What happens when a neutrophil, an immune cell, has to go through a small constriction to get to a target somewhere? How does it remodel its cytoskeleton in order to be able to make it through that constriction?

I think that if we had AI tools at scale to be able to understand all these subcellular compartments, tied to a large language model that would allow biologists to ask those questions just like I said there—because a biologist is never going to have the computational ability to really dig deep into the numbers, but if you can do it like that, and if you have an LLM that you can say, "What happens to the mitochondria when this neutrophil goes through this constriction?"—it would be, I think, an image-based revolution in biology as profound as that molecular biology revolution in the 1950s. I'm not sure we have the tools yet to get there. Someday we will, but it may not be on my watch.

Looking at Life in its Living Form

ZIERLER: Your frustration elsewhere in biology that they're looking at dead stuff, is the message getting through that microscopy is a game changer?

BETZIG: No, it's not getting through. It's not getting through for two reasons. The minor reason is the fact that I'm only one voice. After the Nobel, you're kind of obligated for the first couple years to do the road show, because there are so many people who have helped you in your career and they all invite you. You go on the road show. I had given up on super-resolution five years before I got the Nobel. I was focused on all the live imaging with the lattice light-sheet. I'm trying to give out that message, and I've honed that message even more so since about this—how can you understand life if you don't look at it live? That's what I keep saying. That's my line. I get all these nodding heads and then they go back into their labs and they do their biochemistry.

Incentives! The incentives are to do what you've been doing. It's what you're known for. It's what you do. So, the incentive structure doesn't exist. You have to work your way up Maslow's pyramid high enough to look past your own immediate needs, to have your incentives not be about just you and your career. People get there. Usually when they're older they start working a few levels up, but by then most of their career ship has sailed. What would really be needed is a different incentive structure for younger people to look into this stuff, but it doesn't exist. And it isn't clear that the incentives exist to change the incentives, if you know what I mean.

ZIERLER: The message not landing, your answer skews of course towards academia. What about biotech? Is biotech and translational biology seeing the light?

BETZIG: That's how we got our startup founded, by finding enough VCs who listened to that message. Then our biotech was floundering until—one guy who heard that message was Roger Perlmutter, who was the head of R&D at Merck. He retired from Merck to come run our tiny little startup! Because the message drilled through to him, because he has been banging his head against that wall for his entire career, of trying to look at biochemical stuff to be able to do drug discovery or structural biology! He said, "Oh my god! Yes, this is right!" [laughs] We found a very, very, very small fraction of impactful, flexibly minded people who understand that message, but very few for the amount of effort I've put in so far in trying to spread that message.

ZIERLER: Some history of microscopy questions. Do you see yourself as part of a particular school of thought or intellectual tradition in microscopy?

BETZIG: Like I said, I feel like I am in the Robert Hooke, Antonie van Leeuwenhoek school of microscopists, of developing tools and seeing what I see. Going where no man has gone before by looking at small stuff with it. Discovery. Particularly with the lattice light-sheet I say I have never felt more like Galileo looking with his 30X telescope up and seeing the Galilean satellites for the first time and the phases of Venus and mountains on the Moon than I did with the lattice light-sheet. Because every time somebody brought a sample in, they were seeing their system they had studied for 20 years in a way they had never seen it before. I feel like I'm in the tradition of those guys. I feel like the work that Harald and I did is in the tradition of those guys. I think what we were able to accomplish on his living room floor is a rebuke to all the people who say that, "Those days are gone. You can't do science like that anymore. We all have to work together. We all have to work in big groups." It's not true. I do feel like I'm part of that tradition. I'm proud to be part of that tradition.

ZIERLER: Again, not having mentees yourself, are you missing out in sort of that generational transmission of knowledge, or at least that attitudinal transmission?

BETZIG: You keep coming back to that. You must be a firm believer in this mentorship thing! Because I am not. No, I don't feel like—I give enough talks that there are people in the audience who can hear this message and live this message and learn it. There are some. I do believe I have an impact on some young people and the way they think about science. I think I have some impact on professors. When I give my spiel about everything that is broken about academia, I get a lot of nods from those people too because they're living in. They're as frustrated as anybody. There's sort of a point, I find—when people are assistant professors they just follow the script, because they still have that brass ring that they want to grab that's tenure. Once they get tenure there's this point where they're vulnerable. It's like, okay, I've worked my whole career to get to this point; what do I do now? They've seen the underbelly of what academia is in terms of the grants and the service and all the rest. I see more and more people who really start to reevaluate their career choices right after they get tenure and seriously finally take the blinders off a little. They don't always drop out but there's a surprising fraction of people who go into industry then or make other choices once they've done that. Sometimes they're locked in by family and having to make a paycheck. It's not because they don't understand what they've gotten themselves into.

ZIERLER: We talked about you being an enabler of technology and innovation. What about the other way around? What have been some technologies that you weren't a part of but you immediately grasped their value and the way that you could take it in a new direction?

BETZIG: We've already talked about one, Starship. Just even the Merlin engine and the Raptor engine, those guys are so far ahead it's just not funny. I'd have to think about it, but every now and then I see something that I find inspirational in terms of technology and what people have been able to do. I remember—it's old now, but when the IBM computer was on Jeopardy! and just blew everybody away, that was pretty entertaining! [laughs] Or when they first started beating the chess grandmasters and finally then the Go grandmasters, that's pretty impressive. There's all sorts of things. If I thought about it, I'd think of more. There's always clever people doing clever things. God thank us, the United States is still by far the most dynamic place on Earth for invention and discovery. We do our best to screw it up, but nevertheless there are still plenty of people who believe in the dream and make it happen. Like Jim Allison in immuno-oncology, figuring out checkpoint inhibitors, things like that. Just—all the time. Or the folks who did the mRNA vaccine. Again, you read about most of these people and the way they got ahead was by not having big groups. They worked themselves at the bench to get this stuff done. If you look at the history of Nobel laureates, an amazing fraction of them did most of the work with their own hands. It's not because they led a big group. I don't know why [laughs] people can't see that. It's right there. It's right there. You just have to look at it.

ZIERLER: You talked about the corrosive effects unfortunately of the Nobel Prize. Has the bully pulpit it has offered, because of the message that you want to get across, been worth it for you?

BETZIG: It might be in the future. I really haven't tried to take advantage of the bully pulpit that much yet. Certainly I'm now at an age and a level of frustration where I think I will. Again I've got stories to tell on that bully pulpit. One is that we need this AI, and the other is that energy is the big problem, and we have really misallocated trillions of dollars of resources to try to address climate change and energy. This is not good. [laughs] There are a lot of Nobel laureates who use the bully pulpit for all sorts of things. Nine times out of ten, I feel like, A, it falls on deaf ears, or B, they just reveal themselves as fools because they're trying to act like experts in fields that they're not. I want to be very careful if I make any pronouncements outside of my area of expertise. The message of, "You've got to look at life live," yeah, I use the bully pulpit all the time for that one, but again it doesn't move the needle. It doesn't move the needle because the incentives aren't geared towards that. People will hear the message, they'll nod their heads, and they'll move on. Certainly a plus of the Nobel Prize is the ability to be able to be taken seriously in some quarters for some period of time, but it's something that can wear off pretty damn quick. It's a gun with a few bullets and you want to make sure that you choose your target right before you do that. So, that's a little bit about where I'm thinking right now.

ZIERLER: What's the big message with AI? Obviously everybody is thinking about AI now. There's a ton of hype about what AI is and what it's capable of doing. What's that big message?

BETZIG: Again for me I don't care about those bigger issues. I care about being able to analyze data. That's my focus. That doesn't take me that far out of my area of expertise and my wheelhouse except when I try to speculate about whether AI is even capable of doing that. At least then I give a big caveat that this is just a physicist's three-orders-of-magnitude-error estimate of what is needed. The bigger issues of will AI take over, will AI create misinformation on such a scale that you'll never believe anything ever again, will AI persuade us to do something stupid—all of those are good questions but they're not questions that I feel like I can meaningfully contribute to. I leave that to others to consider.

ZIERLER: What can you meaningfully contribute to in terms of AI and the data that you need help analyzing?

BETZIG: I can tell them exactly what we need out of an AI. I can tell them what has been done with AI in my field so far so they know that. I can talk reasonably conversantly about the latest models and so forth. I would love to have discussions trying to spitball the level of resources required to do what we want to do because I feel like there's still a lot of uncertainty there. I don't see myself actually putting together a model and figuring out [laughs] how many layers I'm going to have [laughs], how many hidden layers I'm going to have in this model, what my cost function exactly is going to be, duh-duh-duh-duh-duh-duh. I'm not diving that deep into it. I will dive as deep as necessary when things work or don't work, but I won't lead it. I want to find good partners for that. It's again one of those things where I can't be completely vertically integrated. I wasn't completely vertically integrated when I did PALM. I wasn't completely vertically integrated when I did high-density data storage. The time to collaborate is when you need—not because, oh, we'll get a bigger grant, or we're more likely to get a grant if we collaborate, which happens too often. No, it's like there's an expertise I need I don't have and I don't think I can get it into my own head, so I need to find somebody who I can mind-meld with, so to speak, on a level and we can communicate back and forth and work together.

ZIERLER: Because the AI world is so big, are there companies or individuals that you have a mind-meld with that are really approaching these questions in the right way?

BETZIG: No, we're talking still the very beginning of this journey for me in this. I would probably try to start at the top and use the shiny medal as much as I can as a way to get my foot in the door. After that, if and when I get a bunch of no's, I'll slowly work my way down the food chain.

ZIERLER: To clarify, your concerns about climate change and the misallocation of all of these funds, do you look at this within your wheelhouse of expertise, or is this more "I have a Nobel, I have this bully pulpit, and I do want to use it in this regard"?

BETZIG: Obviously it's not related to my own research at all. Particularly after reading Smil's book about a year ago it has been a hobby of mine, I guess, to learn about it. I'd like to believe I'm really agnostic about it. I would love solar and wind to be a great solution for everything, but that's not where the data and the arguments have led me so far. I'd like to believe that nuclear is a solution, but I—I rarely give talks now that I'm past that two-year thing because they're just not value added most of the time and I have a family, but I was invited to Oak Ridge, and I went to Oak Ridge and saw the old molten salt reactor and all that stuff. I talked to a lot of the people—a lot of great people, a lot of great expertise in all that stuff there. But again, the people don't want nuclear. That's the fact. It's not a perception that you can change overnight. They're wrong but it is a democracy, and we have to work our way towards ultimately convincing people that this is ultimately the safest solution.

One of the biggest problems in energy and climate is that people don't realize that everything has tradeoffs. They like to focus on what is good about their thing they like and what's bad about everything else. It never works that way. There's always pluses and minuses to everything. It's all about weighing this. Sadly the discourse in the energy field is very political and polarized in a way I sure wish it were not, but it is what it is. Political and polarized is just another way of saying it's incentivized in different directions. It's really hard to beat back against the incentives to reveal the underlying truth behind things. This is the reason why things have to go in a bad direction long enough until things break, and then the incentives change because people realize the cost of the path they went down.

The Dream of Old Science with Future Technology

ZIERLER: As I suspected, this has been phenomenal capturing all of your perspective thematically. We haven't even done any oral history yet about your background and your educational trajectory, so if I might propose, let's meet up again for a round two. I'll leave you with one last question for today. Just to put it all together, it almost seems like you want to operate as a scientist as if you're in the eighteenth century using twenty-second century technology.

BETZIG: That was a very good way to summarize it, yes.

ZIERLER: That's about it? That's where you're coming from?

BETZIG: One of the things I say as an inventor is one of the beautiful things about science and technology—and I saw this so much when coming back after ten years to do the PALM—is that people develop tools for different purposes but they don't realize that those tools can often be used for other purposes they didn't think about. As science and technology go on and there are more and more widgets in the world, there is a hyper-exponential growth of possibilities for further improvement because of the combinatorial things that can happen between all of these things that nobody realized could have connections. Every advance in my career was by putting together pieces of stuff that nobody dreamed would be put together in some way. That's the beautiful thing about science and technology and why, despite everything, the world is better, more prosperous than ever in human history. Despite all of the bitching and moaning that you see, the entire Earth is far better off today than it has ever been, and it is because of the march of science and technology. It gets better faster over time because of these combinatoric associations of what people create.

ZIERLER: Amen to that! Eric, we'll pick up next time. Thank you so much.

BETZIG: All right, good. Thanks, David.

[End of Recording]

ZIERLER: This is David Zierler, Director of the Caltech Heritage Project. It is Friday, April 12, 2024. It is my great pleasure to be back once again with Professor Eric Betzig. Eric, it is awesome to be with you again. Thank you for joining me.

BETZIG: Sure. Thanks for having me, David.

Ann Arbor Upbringing

ZIERLER: Today what we're going to do after our first discussion where we learned all about your unique interests and wide-angle view in science, engineering, physics, biology, chemistry, all of the above, we're going to go back and develop your personal story. I wonder if we can start in Ann Arbor and if your family had a connection with the University of Michigan.

BETZIG: A tenuous one, in a way. My dad went there for his undergrad at the end of the War. He started wrestling in the Navy, and then his coach in the Navy became the coach of the University of Michigan wrestling team. So, my dad was on the wrestling team and ultimately captain of the wrestling team. After he graduated he was an assistant coach on the wrestling team for a number of years. Until probably about 1953 he was affiliated with the University that way.

ZIERLER: Did the research culture of campus rub off on you at all, do you think?

BETZIG: In small ways. Not so much through my family or anything, but because one of the things I would say is the public schools in Ann Arbor were exceptionally good. I think that's partly the influence of the University and professors who had kids in the public schools leading to that. I benefited from that. In the fourth grade, I was already saying, "I want to be a physicist." At that time quarks had just come out. I remember my fourth grade teacher, her husband was I think a postdoc or something in the Physics Department, so I wrote him a letter through her asking, "What's the charge of a quark? What's the mass of a quark?" This kind of thing.

ZIERLER: [laughs]

BETZIG: So, a little bit. I also had a really good friend who—the first guy who turned me on to science, as a matter of fact, in third grade—his father was—I don't know if he was a postdoc or a young assistant professor or whatever, but that was the kid who first ignited the science bug in me. He obviously got it through his father at the University.

ZIERLER: A theme from our last conversation of course is the superficiality of these academic disciplines—chemistry, biology, physics. Do you think even as a boy when you were interested in science, you intuited that there are these walls that really shouldn't exist?

BETZIG: No. I was really narrowly focused on physics from a very early age. From third grade on, it was exactly the inverse. It was like, "I want to be a physicist." Then, "I want to be an astrophysicist." Blah-blah-blah. It really wasn't until I'd say undergraduate years—and again, a little bit influenced by my dad as an engineer and his life—and also just realizing that there were smarter people than me when it came to theoretical physics [laughs], and being a competitive guy, this may not be the best field for me—that I developed a practical bent. That practical bent led to realizing that you can't do anything practical without being interdisciplinary.

ZIERLER: In the late 1960s of course you would have only been eight, nine, ten years old—the campus unrest, the antiwar movement, things like that, were you aware of that? Did that register with you at all?

BETZIG: I was vaguely aware of it but I paid zero attention to it. Certainly Michigan was a hotbed of that but it didn't touch me at all.

ZIERLER: In middle school and in high school, what were your interests? What kinds of extracurricular activities did you do?

BETZIG: I [laughs] read everything about science I possibly could. Tennis would be the only other thing that I got into at that time. I was as nerdy a nerd as you will ever find, and as hyper-focused on learning everything I could about science in general and physics in particular. I read a lot of these Isaac Asimov nonfiction things. He wrote these essays, like one every month or something, in Fantasy and Science Fiction. To this day I still have copies, because they're great essays for general audiences on different science topics.

ZIERLER: Was there AP math and science in your high school?

BETZIG: There was, yeah. I took every AP class you could. I had AP Physics, AP Chemistry, AP Biology, AP Calculus. The AP Biology thing was also very impactful for me, because that guy had never given anybody an A, and I took it as my mission get an A. That was the class that really—it was the first thing that ever really pushed me kind of to my limits. Every week we would do an experiment, and it had to be typewritten. I would usually type about 100 pages, hand it in, pull an all-nighter. My attendance in school was really poor my senior year because I spent so many all-nighters doing my [laughs] AP Biology projects. But it really got into my mind that I'm capable of doing insanely hard work when I want to.

ZIERLER: Did you graduate at or near the top of your class?

BETZIG: Near. I was probably in the top five out of 600 or something like that. There were smarter kids than—in biology maybe not, in physics maybe not, but math there were definitely kids who were brighter than I was. I also took AP English and AP History. I took every AP you could take. I certainly struggled a lot more to keep up with the best students in the humanities ones than in the science ones.

Early Knowledge of Caltech

ZIERLER: Being a precocious fourth grader asking questions about the mass of a quark, just to foreshadow to becoming an undergraduate at Caltech, did you know the names of like Murray Gell-Mann and Feynman growing up?

BETZIG: Oh, sure. Yeah, of course. That was part of the attraction, that those guys were at Caltech. Even though I might never see them, at least they were there. Yes.

ZIERLER: Tell me about other schools that you applied to and why ultimately Caltech won out.

BETZIG: In the end I applied to the University of Michigan, because that was, quote, my "safety" school. I applied to Princeton which I didn't get into. Because of the Institute of Advanced Science and the Plasma Physics Laboratory, I was kind of interested in that. I half applied to University of Chicago. It was a two-part interview process, and the second part you go for an interview. The interviewer asked me what I wanted to do and I said, "I want to be a physicist." He said, "At Chicago, we're interested in all the branches of the tree of knowledge, and you have to sample all the branches." I said, "Thank you very much, but this is not for me." [laughs] Caltech was far and away my number one choice so I was ecstatic when I learned I got in.

ZIERLER: Were you well-traveled growing up? Had you been as far west as California?

BETZIG: No. That trip to Chicago was as far west as I had been.

ZIERLER: [laughs]

BETZIG: And that's from Michigan, you understand. I drove out to Caltech with some sophomores who were in Ann Arbor my freshman year. That was the first time I ever went west of the Mississippi.

ZIERLER: Was there a faculty representative who came out to meet you in Ann Arbor? Was that part of the application process?

BETZIG: Yes, yes, there was, as part of the interview. He was in Chemistry. Dervan or something? I can't remember his name right now.

ZIERLER: Peter Dervan.

BETZIG: Okay, well, that's it. Yes! That was the guy who interviewed me.

ZIERLER: Oh my goodness, that's incredible. All right! What were your impressions? What was it like when you arrived in Pasadena?

BETZIG: Scary, of course. I was introverted to the point of unhealthiness, I'd say. I was so introverted I could not go into a fast food restaurant and order a meal. I had to have my sister or brother do that for me. I was terrified of about everything. I remember we came early because the sophomores, one of them was on the water polo team and they start their practices before the semester starts. Before the figuring out which house you're going to be in, I was temporarily in Page House. Basically, I just holed myself up in that room for two and a half weeks or whatever. [laughs] That's where I was! When the classes started—I never have a problem contributing in a class. It's just outside of the class. Then of course that led to me eventually opening up some degree even outside of the class when I ended up in Ruddock and I realized there were some people who were even more eccentric than I was, so [laughs] I didn't need to feel bad about it.

Quantum Mechanics and Thermodynamics

ZIERLER: The first two years it's a pretty general curriculum. You get exposed to everything. What really resonated with you?

BETZIG: It was really as a sophomore that there were a few things that started—the freshman year is really baked in. I was really scared that I would be underprepared and I had always poo-pooed my high school, but once I saw what I was taking in freshman year I said, "I've done all this. I know all this." Other kids were struggling, and to me, freshman year was kind of a review. There wasn't much I didn't know. Sophomore year things certainly picked up. I took a course in applied physics. I took a lot of quantum mechanics courses. There was one in applied physics by—god, I can't remember the guy's name right now. I really liked him, too. That was an overview of its applications in different things that that was good. We had to take, as part of the physics track, thermodynamics, which was taught by Hans Liepmann. I loved Hans and I loved his class. He never went from notes at all. He just derived everything right on the board, right out of his head. He lived and breathed it. I took the midterm and that was the first time I ever failed [laughs] anything in my life. I was so petrified [laughs] on that. I managed to pull an A out of the class in the end, because it certainly put the fire in me to turn that around. Hans was great. I used him as a mentor pretty much for the rest of my time at Caltech.

ZIERLER: How much biology did you do as an undergraduate?

BETZIG: Very, very little, actually. Did I take any biology classes in undergrad? I don't think so. I definitely started to steer a little—taking a sampling of things in applied physics. The other thing that happened, in part because of Hans, is that that was the first year of the SURF program, and I got a SURF fellowship. I had taken a sophomore elective class in engineering and one of the projects was a fluid mechanics project. That professor, Brad Sturtevant and Hans recommended me to another guy who was interested in taking on an undergraduate, and I had the fellowship. Garry Brown was the guy I worked for, in GALCIT. I started working with a graduate student who graduated and I kind of carried it on myself more in junior years. It was a really good project. It was looking at instability modes in jets and a flowing exhaust from a tube. We would put on a magnetic field and deform the tube to excite different modes of oscillation in the jet and use a hot-water anemometer to measure it. It was my first serious exposure to doing experimental research and I loved it. I really loved it and I was good at it. [laughs] It was a marriage made—it didn't matter what I was doing; as long as I was building things and making measurements, I found my calling at that point.

Professor Brown was also a great mentor. He was another one of these guys—when I'm trying to understand how these modes of oscillation happen, he starts writing on his board. He starts writing curl and divergence, this, that, [laughs] and I'm lost within two minutes. Then he says, "And see? See? Isn't that simple?" [laughs] Like, whatever! He was super bright. The other thing I learned from Dr. Brown was—in my junior year after I had done two summers of that, Caltech had an affiliation with the American Institute of Aeronautics and Astronautics, and a number of professors and graduate students, postdocs were involved in that. They also had an undergraduate division where they would allow undergraduates to give scientific talks to get them up to speed on what it's like to do that sort of thing. I prepared a talk. Like I said, I was super introverted, but somehow whenever I go onto a stage I become a major extrovert. I thought I prepared a really good talk and then I gave a practice talk for Dr. Brown, and he just tore it to shreds. [laughs] He said, "Way too much information. Way too small. Crappy graphics." This, that, and the other thing. "You can't expect everybody to know everything you know. You have to justify it better and motivate it better." Blah-blah-blah-blah-blah. To this day I still think that one of my real strengths is in public speaking and giving scientific talks. I can usually get an audience to resonate with me really, really well. I really trace that all the way back to Dr. Brown.

ZIERLER: Oh, wow.

BETZIG: He's the guy who told me how to do that.

ZIERLER: This self-realization that you were good with experimentation, that obviously you must have been good with your hands—growing up, were you a tinkerer? Did you have chemistry sets?

BETZIG: A little bit. Like I said, with that other kid in the third grade, I started tinkering a bit. There was something called Science Service back then that would send you a kit for an experiment every month. We would make a battery on-e month, something else the next. By seventh grade, the science teacher would let us go into his back room where he had all the chemicals and we'd make explosives and stuff and play with the Van de Graaff generator and do stuff like that. I started playing with circuits a little later. Yeah, just a smattering of—but I did learn that I really, really liked to design and build things. From a very early age, I was pretty much an inventor. I still characterize myself as an inventor more than anything else.

ZIERLER: The rude awakening that perhaps theoretical physics was not for you, did you get to interact with Feynman or Gell-Mann at all? Did you take classes from them?

BETZIG: Feynman a little bit. First off, of course he always went to the orientation on Catalina, so I heard him talk there. He also had the Physics X going on there, where he would just have freshmen come in and ask him questions. Those were my two experiences. I can't even remember what I asked him, but I asked him one question once. I've since come to appreciate and love him much more from Surely You're Joking and the other things that make him a much more human person to me than I thought at the time. He was probably the only one. Garry Brown and Hans Liepmann were probably the two guys that I had the closest connection to on the faculty.

ZIERLER: Did you stay on campus for research during the summers?

BETZIG: Yes, as part of—SURF was new sophomore year. I did that sophomore, junior—and senior year was different because I almost flunked out of Caltech after my junior year.

The Caltech Crucible

ZIERLER: Oh, no. What happened?

BETZIG: What happened is I was starting to take harder and harder physics courses. I never got over this idea that if I don't get an A, I'm a failure. I had a 4.0 going up to second semester of junior year. The firehose was, man, just streaming [laughs] really fast at that time, faster than I could take. I really was on such a treadmill of just work, work, work, work, work, literally around the clock, no time to think, and it ruined my health. I developed this eczema so my entire face was actually oozing pus. My hair was falling out. It was really intense. Hans Liepmann looked at me and said, "You need to back off." [laughs] So I took the third trimester off, because between AMA 95 and I think it was Physics 118, Quantum Mechanics with Cohen-Tannoudji, and some other things, it was just too much, too fast, to get an A on, and it just kind of broke me down. I took that trimester off, and in the summer I went to Europe and just bummed around and did nothing, climbed mountains. I also gained a lot of weight with the stress of school and I lost all that weight over the summer. I came back with a desire to get the hell out of there. It kind of switched to, "Finish it off and get the hell out of there." Also, "Don't kill yourself for an [laughs] A. You don't have to." Senior year, I just did my stuff, A's and B's. I was still some units short of the amount you need to graduate, so I worked the summer after my senior year there. I only had to take one class to meet the unit requirements. I actually went to Cornell on the same schedule I would if I had graduated on time, but as a result I'm an alumnus of the class of 1983 even though I consider myself a class of 1982 and all my friends are class of 1982.

ZIERLER: With all of the difficulty, all of the stress, almost failing out, did you ever think about not pursuing graduate school, not going the academic route?

BETZIG: No. I always knew I wanted graduate school. Up until that flameout thing, my real goal was to either become an astrophysicist in the Kip Thorne mold, or become an astronaut. I had a pilot's license in high school so I was thinking maybe I would do a military thing or something and try to get towards. But the shuttle was—I knew the time STS-1 went off that that thing was a horrible white elephant and a boondoggle. It was my first introduction—I mean, I love space. I still could name you every astronaut in the Apollo, Gemini era, and all of that. I'm still a huge space buff, but it was my first understanding that the way the world works is not the way the world should work. Understanding that keeping contractors funded was more important than building the right type of space vehicle, that was my first introduction that politics trumps science in some ways like that. Therefore I pivoted from that. Thanks to what I did in the lab, I was thinking that I wanted to do applied work, applied physics. Astrophysics was out. Astronaut was out. What's next? Applied physics. Where do they do applied physics? At that time there were only two programs for applied physics in the country. One was at Stanford and the other was at Cornell. I hated Pasadena. I live in California; I still hate it. I do not like this state. It's a beautiful state, nothing wrong with it that getting rid of 80 percent of the people wouldn't cure—

ZIERLER: [laughs]

BETZIG: —so that it has a reasonable population. So, I didn't want to go to Stanford. And I wanted to go someplace where the male-female ratio was 50/50. So, I went to Cornell. I figured I needed to learn how to talk to a female at some point, and still by senior year I could not look a female in the eye and talk.

ZIERLER: Right, because Caltech had only been coed for eight or nine years by the time you arrived.

BETZIG: My entering class was 210 and nine of them were women, yes. I felt sorry for them. I didn't want to talk to them because God knows they got far too much attention as it was! I would have hated that [laughs] if I were them.

ZIERLER: Thinking about being an astronaut or astrophysics, as an undergraduate did you have any interface with JPL? Were you aware of its connection to Caltech?

BETZIG: Of course. In fact, one of my fondest memories is—another course that was very influential for me was an elective I took sophomore year, an optics course taught by Bill Bridges. That was in that old EE building just across from Ruddock, Steele. They did plasma physics in there too. They had a closed-circuit connection with JPL so we were watching the pictures come from Voyager 1 and 2 as we're taking the class, live, as they were coming into JPL. We were the first to see like volcanoes on Io and stuff like that. That was awfully cool. That was very influential. I was thinking of that as possibly a long-term career, even though I didn't get out to JPL. It still interests me, the idea of working on spacecraft, because of my tinkering. The amount of space astronomy we're going to get [laughs] coming up when Starship is running routinely—screw the TMT! I mean, that's completely archaic! Put your fucking 10-meter scope in orbit or at L2 like the Webb or even much bigger than the Webb! I mean, it's stupid to think of a large ground-based telescope anymore because in a few years they'll be able to do much—and the planetary astronomy! God, you'll be able to send a 50-ton spacecraft anywhere you want to go! Think of the science you can do with that. We're going to enter—

ZIERLER: Because the propulsion is so powerful now?

BETZIG: Because they can move so much more mass to orbit at a much lower price. It also means that you're not trying to shave milligrams off your damn spacecraft and making it like a—it was nearly a miracle that Webb was able to go up and deploy its mirror without failure and its sunshield. You're not going to have to do that kind of crazy optimization anymore. It's going to change everything.

Initial Entry to Optics

ZIERLER: You mentioned Bridges and optics. That prefaces my question about seeing in your undergraduate education at Caltech if there's any foreshadowing to microscopy. It wouldn't have been through biology. It would have been optics?

BETZIG: Yes, correct. That's exactly where I saw—Bill Bridges' class was very influential for me as well. One particular thing that he showed is—because he did classified work for Hughes, one thing that was recently unclassified that he had done was something called COAT, Coherent Optical Adaptive Technique. I forget what the acronym is, but it was adaptive optics. He showed us a video that they took at Hughes where they had a model of the Starship Enterprise and they put like a hair dryer in front of it to roil the atmosphere and then shined an infrared laser through that. It's all scrambled up and then they turn on the adaptive optics and it focuses right on the bridge of the Enterprise, and they can move the model and the laser tracks it. Adaptive optics became super key to me later in my career by applying it to microscopy. From that day in probably 1979 I was thinking, "Somebody, somehow, I'm going to use adaptive optics." [laughs]

ZIERLER: Given that there were only two applied physics programs to consider—Cornell and Stanford—where did applied physics sit vis a vis electrical engineering programs?

BETZIG: It was substantially different. At least those two programs did not just encompass semiconductors and shit like that. I don't know a lot about the Stanford program, but one guy I learned to later admire was Cal Quate, who did some microscopy, sort of an acoustic microscope. He also was coinventor of the atomic force microscope and stuff. None of that has anything to do really with EE per se. Likewise at Cornell there was a plasma physics guy, there was a guy developing new lasers, new types of gas lasers. There was a variety of things that were really truly applied physics. That's where I went.

ZIERLER: Was it a joint program for you between Engineering Physics and Applied Physics?

BETZIG: At Cornell, no, it's its own department. The Department of Applied and Engineering Physics was its name.

ZIERLER: The idea—I know I've heard this before—Cornell applies itself in Engineering Physics because you get as much engineering as you do physics. It's almost like two for the price of one.

BETZIG: Yeah. I'd say there was a heavy bent on it.

ZIERLER: I wonder, going to Ithaca, if it felt very similar to Ann Arbor, and that was a good thing for you.

BETZIG: It did, and I appreciated that. To this day I love Ann Arbor. I wish I could live in Ann Arbor. Most of my family is still in Ann Arbor. It's a great town and a great part of the country. I love Ithaca just as much. It's much smaller than Ann Arbor, but it is even more beautiful because of the gorges and the hills and so on. I loved Upstate New York. It was great.

Applied and Engineering Physics at Cornell

ZIERLER: How well-formed were your research ideas entering the program at Cornell?

BETZIG: At the very beginning, not at all. I went in completely agnostic about what I would work on. I looked at what was happening in the Department and I latched onto what I ended up doing for the next 12 years almost immediately. As a kid, I grew up with Apollo. I grew up with Star Trek. I always believed that science and technology is ultimately a force for good, and everything that we cherish in our lives today is a result of that. I wanted to contribute practical things that would make people's lives better, and something impactful. I wanted to do something important. These guys had this idea to make an optical microscope that could look at living cells with the resolution of an electron microscope. If you state it like that, the potential impact is obvious. Everything else in the university seemed tame compared to something of that significance. It was an easy decision.

ZIERLER: When you say latching on, what were the research groups that were involved in this?

BETZIG: There were two. One was a young associate professor called Mike Isaacson, who had come out of the University of Chicago, which had a very storied history in the development of electron microscopy. He was doing scanning transmission electron microscopy, first for imaging. He, with Elmar Zeitler, were the first to image atoms with electron microscopy. Then Mike at Cornell—Cornell had just recently started what was then called the Microfabrication Facility and eventually became the National Nanofabrication Facility, and on and on. Basically he was using his EM to do lithography and trying to show he could make small structures in silicon nitride membranes with that.

The other guy was another young associate professor, Aaron Lewis, who was a Raman spectroscopist. Since lasers powerful enough to do Raman spectroscopy were still fairly new, it was considered pretty high-tech to do Raman spectroscopy at the time. Mike and Aaron had conceived of the idea of using Mike's microscope to lithographically make holes much smaller than the wavelength of light in a membrane, and then coat the membrane with an opaque metal, and then use Aaron's laser to shine light on one side of the hole, and then the light that comes out the other side of the hole is then restricted to the size of the hole instead of the wavelength. Since that hole is much smaller than the wavelength of light, you now have a nano flashlight. If you could drive that as a nano flashlight across a surface point by point, you would get an image at resolution based on the size of the hole instead of the wavelength. So, a super-resolution microscope. Ultimately we called it near-field scanning optical microscopy or NSOM.

Lasers and Little Holes

ZIERLER: If we could back up a little bit, on the technology side both for the optics and the lasers, what were some of the breakthrough technological developments that allowed for this?

BETZIG: The big breakthrough first was being able to make holes that small, which was Mike's bailiwick, which was basically scanning transmission electron microscopy. Now, because the light through the holes is very inefficient, you need a bright light source. At that time, it was argon ion gas lasers that were very big and very expensive. That's what we started with. The other key ingredient at that time was the ability to automate an experiment. Because PCs were—I controlled my microscope with two IBM ATs. I started with IBM PCs. I started with 8088s and I ended up with 8286s by the time I graduated.

ZIERLER: I wonder if you could explain the distinction in those two computers.

BETZIG: One was an eight-bit processor, and then a 16-bit processor when we got to the 8286. God, I can't remember what the clock rate was but it was in the single megahertz numbers. [laughs] But that was a long way from having to control an experiment yourself, so this is a big deal! It was a really, really good thing—it worked out almost perfectly—because there was already another grad student who was on the project, Alec Haratounian. I kind of horned my way in. Alec was nearing completion. It turned out that those membranes that those little apertures were in, they're 100-nanometer thick silicon nitride [laughs] so if you look at them the wrong way, they break. If you try to bring them close to a surface to image something, they break. So it really wasn't plausible. Then Alec had a real great idea, because he had friends working for Watt Webb down in the basement.

ZIERLER: Oh, yeah!

BETZIG: One of the hot things then, because of Neher and Sakmann, was doing electrophysiology with tapered micropipettes to make a tiny little hole that you patch-clamp then on a channel in the membrane, and then you can make measurements of ion flow through the channels of the membrane. Alec said, "It's really easy to pull these pipettes. What if we coat those with metal?" That became the practical way by which we then did the near-field. Alec got to the point of being able to do an initial sort of one-dimensional thing on an edge to say the edge is sharper. Then he graduated, and I built sort of this big microscope to do two-dimensional imaging. I had to do the other really key thing, which was find a feedback mechanism to control the distance from the tip and the surface, because the light out of that hole spreads super rapidly, and if you're more than 20 nanometers away from the surface, forget it. You have to be really close.

That was a great opportunity. Mike and Aaron were busy. They were chasing tenure and [laughs] all the rest. They had many, many other projects. I knew just as much or as little as they did about what was needed for the project. I worked really hard and I was pretty bright, and so they left me alone. We were lucky enough to get an Air Force grant—my first year I was lucky because we had no money, and I learned how to do science with no resources. Then about two or two and a half years in, we got this grant to build this full-blown microscope, and I was lucky because now I had money, and I had infinite freedom. Everybody left me alone to just do it. I learned so much, you cannot believe. I learned how to be a scientist and an engineer. I learned how to machine. I learned how to do electronics. I learned how to do programming. I learned everything.

ZIERLER: From our first conversation—this is probably also where you appreciated the value of small science, of doing it on your own, not part of an enormous team.

BETZIG: Absolutely. Absolutely. I could be completely vertically integrated within myself and still successful. Yeah, you're absolutely right. That burned something into me to believe that this is the way. Yes.

ZIERLER: You must have been really lucky in your appreciation of how to be scrappy when you had no money, and then you can take those skills when you do have the resources.

BETZIG: Right, and I've learned since that having too much money in an organization is just as deadly as having too little. There's a sweet spot.

ZIERLER: Did you get to know Watt Webb at all?

BETZIG: A little bit. He was—imperious, let's say. He was not an easy guy to get to know. He was the one guy always wearing his suit and tie and acting fairly—he always seemed to get the best people. Winfried Denk was a colleague of mine, and there were others who were just—he had three or four people who are certainly National Academy type level at that time. But he was a hard guy to get to know. I did have one interesting run-in with him. At the beginning, he didn't believe in near-field at all. Then one time I met him and he kind of asked me—I explained, "Well, it's just a wave guide that's below cutoff. Yes, it's inefficient, but as long as the channel isn't that long, you're going to get some photons." Eventually he kind of came around. I don't want to speak ill, but I think he was always, after that, kind of a little bit bummed that it wasn't his thing. [laughs]

One time, my girlfriend, later my wife—who I met there, she was also in the Department—at some point they wanted to kick her out because they didn't think she was good enough. This was crap. It was just an argument with the guy she was TA'ing for. Webb was department chair then, and I went into his office and said, "If you kick her out of the Department for this, I'll just take my business elsewhere." [laughs] And boy, he—just his eyes went [laughs] like this. "You think this is a business?" I said, "Yeah. I do." [laughs]

ZIERLER: Wow.

BETZIG: [laughs]

ZIERLER: It worked!

BETZIG: I don't think I had anything to do with it, but I think in the end they realized that it wasn't the right thing for them to do. I didn't have any sway at that time. I'm just happy that it worked out.

ZIERLER: What was the dynamic between you and Mike and Aaron?

BETZIG: Hoo, that's another [laughs]—I'm not an easy person to get along with, particularly when I'm fully into something, and I was fully into that. Mike and I had a fairly good relationship throughout. I started off actually as Aaron's student. I would say I was just kind of an asshole. I went into graduate school revering professors and "these people just know everything and I know nothing." By the end of year two, I kind of felt the inverse. I said, "Why are these guys driving the boat? [laughs] I know a lot more than they know!" I would listen to them talk and I'd say, "What you're saying isn't right! [laughs] You've got this wrong." Mike was a very solid scientist. Aaron was solid in his own way, but Aaron was—a showman. Mike couldn't sell anything but Aaron could sell. Mike could do science and Aaron could sell. But Aaron would sell way beyond the laws [laughs] of physics allows. I dislike this idea of losing that truthfulness or trustworthiness. Anyway, we had grand plans, the three of us, to start a company to build near-field microscopes. We had some patents and so forth that we had done. At that time, Aaron also decided to do a sabbatical at Hebrew University in Israel.

ZIERLER: Was the Air Force grant supporting basic science?

BETZIG: Yeah, it was a basic science grant. That's all.

ZIERLER: There wasn't a national security component to this, nothing like that?

BETZIG: No. It's the Air Force office of Scientific Research, which does all sorts of general far-reaching R&D.

Pushing Against Theoretical Limits

ZIERLER: I wonder if you can talk about the way that these experiments pushed up against theory and theoretical limits in optics and microscopy.

BETZIG: Yeah. One of the very first things I did before I even built the microscope in that year when we didn't have money is I used an IBM PC 8088 to do an electromagnetic calculation of how light would go through a sub-wavelength hole in a perfect screen, a conductive screen. That informed quite a bit about how short the near-field really is, which as I learned in the end is really its Achilles heel that limits its use. I knew it then theoretically, but I found out practically. Because of all the theory I had at Caltech, I could model things really well. I understood the electromagnetism better than anybody—what the principles were, what the materials, how the material properties affect what happens, and all of that kind of thing. Then it was just a matter of making it.

ZIERLER: Your graduate research, what aspects would you say were more of a technology demonstration and where was this a tool that answered scientific questions?

BETZIG: As far as I got was technology demonstration. We used Mike's e-beam lithography to make test patterns, gratings that are smaller than the wavelength of light, or writing Cornell NSOM, Near-field Scanning Optical Microscopy, smaller than the wavelength of light, and then reading it out with light in the microscope. That was my thesis, doing stuff like that.

ZIERLER: In thinking about starting a company, what would be the product and who would be the end user?

BETZIG: The idea is that light as a tool for inspection is incredibly powerful. You have fluorescence for biology. You have spectroscopy for materials. There's lithography that you can do as well, so you can do super-resolution lithography. Optical data storage was a thing. You could do super-resolution data storage. The potential applications are very, very broad. That was what attracted me to it. If you think of all the things in our world that are done still today with optics and light and imaging, and think of doing that all at ten times higher resolution, it doesn't take you long to figure that there's a lot of potential.

ZIERLER: Tell me about the thesis defense. Was it contentious at all?

BETZIG: No, not really. Being me, my thesis is two volumes, each about this thick. I had the largest thesis I think in the history of Cornell University.

ZIERLER: [laughs]

BETZIG: Lots of images. Every little circuit that I built. I exhaustively documented that whole microscope. I was fortunate enough to have just enough money that I didn't have to type it myself. At that time, Wang word processors were a thing, so I hired some woman to type it all in. It was called Nondestructive Optical Imaging of Surfaces with 500 Angstrom Resolution. That was the title of my thesis.

ZIERLER: Have you revisited it? Has it held up?

BETZIG: It's still valid and holds up. There are plenty of people doing near-field microscopy today. It's a field. It's just really limited by the fact that your probe has got to be exceptionally close to that surface, and the probe is big compared to the separation, and so you have to have a pretty damn flat surface where the thing you want to look at better be 20 nanometers or so [laughs] from the surface. It's a surface tool and that's it. Flat surfaces, at that.

ZIERLER: In the 1980s was the term "nanoscience" in use?

BETZIG: Probably at the very end, it was starting to, thanks to STM. That won the Nobel in 1986. Nano started to enter the lingo in the 1980s. Certainly by the 1990s I was sick of hearing nano-everything. Yeah, it was starting its exponential rise at that time.

Starting at Bell

ZIERLER: Now we can think about moving the story to Bell Laboratories. Obviously Bell's storied history, all of the incredible work that had happened there, the breakup of Bell Labs and Judge Greene, were you following that story and the impact that this had on AT&T?

BETZIG: Not at all. In fact, Bell Labs wasn't even on my radar until the very end of graduate school. I was supported in my final two years by a fellowship that came from IBM Watson. As part of that, I made a couple trips to their scan probe group in Yorktown Heights. I figured that was where I was going to end up, as part of that group. I was focused on that. They had the best group in the world in my opinion in terms of scanned probe microscopy at the time. But in my final year, Bell Labs was considered the holy grail of the real condensed matter physicists at Cornell and the low-temperature physicists in particular at Cornell. They all wanted jobs at Murray Hill. It wasn't on my radar.

The way Bell worked then—and this was a great model—the way they tried to attract talent is they would have people go back to the universities from where they got their PhD once a year, and they would just walk the halls and talk to graduate students. They started identifying the stars pretty early—year two and year three—and every year they go back and see, "How are you doin?" If they were good, they would invite them for interviews when they were done. I was not part of that. Most of that happened in the basement of the building, where the real physics happened instead of the applied physics stuff where I was. But they had an open-door policy on one of the days, and so I went in there with—not my thesis but a big binder full of all of my images and my microscope and all this stuff. Of course I was quite passionate about it, enough to convince them to give me an interview.

Then I went to the interview. The interview was one of the best times I ever had. Again, I didn't know anybody there. They asked me to prepare an hour talk, and the talk took me like two hours and 15 minutes to give because I was just hammered with question after question after question, just interruption after interruption. I absolutely loved it. It meant they cared. I could handle—they were so smart they could probe exactly where the weaknesses were. I could defend what I could defend. I could not defend the things I couldn't defend, and I would say so. I'd say, "I think this, but I'm not sure. If I came here I'd like to try to find out by doing this." The canonical question they ask at the end is, "What would you do if you had an empty room?" I told them what I'd do if I had an empty room.

One of the guys in that audience was the head of the semiconductor physics research department. His name was Horst Störmer. I didn't know a hole from an electron to save my life. I didn't know what a band gap was. Well, I had taken a solid state physics course, but still, my knowledge compared to those guys of semiconductor physics was negligible. Yet Horst kind of figured, "Man, if we could just do optical spectroscopy like we do with diffraction limited of these heterostructures we make, if we could do that at 100 nanometer or better resolution, we could learn a lot." So, I ended up in the semiconductor physics research department as the one guy who didn't know any semiconductor physics. Horst was the best boss I ever had. It was just fantastic. That's where I met my friend Harald. He was also in that department. He had been hired by Horst two years earlier. We had so much in common. We're both from the Midwest, we're both doing scan-probe microscopy which has a lot of commonality, and we're both in the same department. Horst was supportive like crazy throughout the entire time I was there. Bright as a whip. Super energetic. Charismatic. One of the most charismatic men I've ever met. Then he won the Nobel in 1998 for fractional quantum Hall.

When I got there in 1988, even though the breakup was 1984, it still hadn't really permeated at all through the organization. I think in the last interview, I told you about this hierarchy from somebody telling me, "You've got to publish PRLs" until my applied work is sort of the paradigm by which people were judged, until Harold is looking at fruit in the supermarket checkout. That was how quick the culture changed in the six years that I was there. But the entire time I was there, I was untouched by that, and it was just great. Absolutely great. I just hauled ass while I was there. It was the right amount of resources. The rooms were dark and dingy. There was a good budget but a limited budget. Every paper I did out of there was a different set of collaborators, because near-field had so many different applications. People started to get to know me. I'd walk around the halls, and all of a sudden I'm doing high-density data storage, and then I am doing semiconductor spectroscopy, and then I am doing membrane biophysics, and then—it was fantastic. Still the best time of my life! [laughs]

ZIERLER: Considering initially IBM and then ultimately ending up in Bell Labs, were you self-consciously not looking for a faculty appointment?

BETZIG: Yeah, I had no interest in that. I had already learned what being a professor was all about. The one thing it's not about is being in the lab and doing research! [laughs] That's what I wanted to do. I always wanted to do research. I always wanted to do things with my own hands. I had zero interest by the time I graduated of like doing a postdoc or—it was probably going to be either IBM or Bell. In the end, I went Bell.

ZIERLER: Beyond all of the benefits of the collaborations that are going to push you in new directions, going back to this idea of what would you do if you had an empty room, how much of what you wanted to do on your own did you see as a continuation of your work at Cornell?

BETZIG: It was a clear continuation. It was. I was just picking up right where I left off. I just felt like the story wasn't done yet.

ZIERLER: That begs the question, what was the unfinished work? Where could you take this?

BETZIG: First, to build a better microscope, which I did in a number of factors. I made a new kind of probe based on optical fiber that got me 10,000 times as much light through the hole as I had before. I had a feedback mechanism that was really robust and noninvasive that I could track that over rough surfaces. Then it was all applications. Applications, applications, applications. It was a great place to be, because there was no focus in the physical research division. People still don't understand the value of that, of having it so that—and the labs are so small. You have a hundred different topics in science by 200 people! It's all over the map. That was perfect for near-field because there was such a broad array of applications. It was perfect.

The Jump into Membrane Biophysics

ZIERLER: What was great about having all of those new collaborators? You mentioned membrane biophysics. This was probably your first serious work in biology?

BETZIG: Damn straight, yes! [laughs] Dave Tank and Winfried Denk and those guys, I was learning from them. I got through them connections to outside people in academia like Michael Edinin at Johns Hopkins and others. Then we go off to the races. Like I say, I didn't know three months in advance where I'd be using that microscope next, but I knew that there was no dearth of things to do with it.

ZIERLER: This basic science nirvana that you experienced for these six years—this is obviously going to be above your pay grade, but who were some of the heroes who were able to keep that culture of Bell Labs alive after the breakup? How was that possible?

BETZIG: Because the funding was still there. Bellcore didn't really split off from Bell Labs until around 1988. Basically the parent organization was still very much in favor of the support. 1992 or 1993, that's when the brass bought National Cash Register, and there was definitely a change of environment after that point. It was more about we have to harness the research to do practical things that would help NCR or help stock price. Then 1994ish is when they actually broke up Bell into different parts. Our part was called Lucent Technologies. That was then the runup through the dot-com boom, and Lucent became, like an Nvidia today, one of the high flyers. Then it crashed and burned when the dot-com bubble burst. Things became much more driven towards the marketplace starting I'd say after 1992. I left in 1994. Before that, it was really still very pure. Horst eventually became head of the physical research division, where most of the basic research was done. Above him was Bill Brinkman with the physical research division. Bill was an old physicist who also kept things going. At the top of that was Arno Penzias. Arno was supportive. The decision wasn't in their hands anymore after around 1992 and certainly not by 1994. Every year it was kind of like this effort to beat back the barbarians [laughs] who were trying to change the culture. Horst, being the most energetic and persuasive guy I know, you could kind of start to see everybody was starting to feel a little bit of the weight of the world on their shoulders towards the end of my time there.

ZIERLER: At Cornell, as you were saying, the focus was really on the technology demonstration. Was it at Bell Labs when you started to think about science objectives, what you could do with this technology?

BETZIG: I was never interested in technology for technology's sake. I always wanted to see what it could do and find out what it could do that would be useful. It's just that it took six years to get it to the point where it worked well enough to get it a job at Bell Labs. Then it was going to the next chapter, which was the application. Again, I couldn't have been in a better place to demonstrate those applications.

ZIERLER: We should talk about the Abbe limit and its relevance here.

BETZIG: Again, before that, it was believed that you cannot probe or measure or image things smaller than half the wavelength of light, which is the Abbe limit. The near-field holes we were making were on the order of five to ten times smaller than that, and getting to be that much higher resolution. The reason it doesn't break Abbe's law is Abbe's law is absolutely true if you're making your measurements and your imaging device is more than a fraction of a wavelength away. But when you get super close to the specimen, there are other electromagnetic fields which don't propagate but are evanescent. They decay exponentially with distance. The information decays exponentially with distance. If you're close enough within a fraction of the evanescent decay length, then you recover that information. By putting a sub-wavelength hole a fraction of a wavelength away, you can get that. That's the loophole that near-field exploited to Abbe's law.

ZIERLER: Is Moore's Law relevant here? Does Moore's Law trump Abbe's limit?

BETZIG: Not exactly. As they push-push-pushed further in size in semiconductors, they've certainly done things that bounce right up against Abbe's law. They do everything they can. They use the shortest possible wavelength they can. They use the highest refractive index photoresist they can. They use phase shifting mass to get a little bit more beyond that. There's little tricks you can do like up to a factor of two if you have patterned excitation, which was eventually exploited in biology as structured illumination microscopy. The same kind of tricks can be exploited in biology but still it's tethered to Abbe's Law. Nowadays, they use EUV lithography, but they put a water bead in vacuum, levitate it, and they zap it with an excimer laser and it creates soft X-rays that then are the light source, which are then bounced off of these crazy reflective mirrors that reflect X-rays very well. Then they focus all of that at TSMC to make five- and three-nanometer linewidths. But we're not going much beyond that. I think you can safely say that Moore's Law is hitting its wall at last.

Optical Wells and Thermal Broadening

ZIERLER: What is the relevance of the temperatures that you're operating at? From absolute zero to room temperature, what are the considerations there?

BETZIG: It depends on the application. Most of my stuff was at room temperature except for an experiment that I did with Harald. In that case, we were looking at how electrons and holes combine as excitons collapse to form light in a semiconductor quantum well, which is what is used in like semiconductor lasers. That's how you create the emission. Because those linewidths are broadened by temperature, the only way you can see the individual linewidths of single excitons is by being cold enough that the thermal broadening is negligible. That's why you've got to go to like two degrees Kelvin. In the experiment I did with Harald, we put my near-field probe in his low-temperature scanning tunneling microscope and then studied these quantum wells that were made by Horst and Loren Pfeiffer and Ken West, who had the best MBE system in the world to make the purest gallium arsenide to make the best quantum wells. Everybody of those hundred people was the best in the world at this, that, and the other thing. You bring combinations of them together and you do research that nobody could do anywhere else on the planet.

ZIERLER: When you started to get frustrated—the counterfactual is, had the culture not changed, you would have happily stayed at Bell Labs for a career?

BETZIG: No, no, no, because at that time I had come full circle. Remember I said when I went into graduate school it was the idea of making an optical microscope with the resolution of an electron microscope to look at living cells? That was always the end goal for me. Near-field was never going to be able to do that because of that short depth of field. Cells are too rough compared to the scale of near-field. Most everything you want to see is beyond the plasma membrane and what you can access. Basically near-field is good, like I said, for flat surfaces and where the thing you want to see is within 20 nanometers of that flat surface. Guess what? I personally exhausted every freakin possible application which ends up falling within those constraints. I did em all! There were no more to do! [laughs] If I were going to stay I would have to completely pivot to something new. A, I didn't have any idea. B, I was starting to feel that culture change. I could feel that people were feeling under pressure because of that culture change. So, staying and trying to restart a new basic science field under those conditions—I mean, Horst said, "Take some time off. Just think. You don't have to leave. You can figure out something new here."

The other thing, too, was I was just exhausted. Again. Just like at Caltech. Not to the hair falling out and eczema thing, but I worked—Harald and I would come into work every morning at 4:30. We were best friends but hypercompetitive, so that if he beat me or I beat him, the other would put their hand on the hood on the other guy's car to find out how many minutes they beat them by. Then we would go in and we'd work until the sun rises. Then we'd go play tennis. Then we'd come back and we'd work until 6:00. Then we'd go to the same Chinese restaurant every night and eat dinner. Then we'd go back into the lab until 10:00. Then repeat, seven days a week. I did that for six years. I loved it, but—it was enough. It was time to reboot. I had no idea what I was going to do.

The other thing that took me away from near-field was it was—again, my first—I told you about my first understanding that the world doesn't work in a logical way with the space shuttle, right? Well, I learned that academia doesn't work logically either. Because when I first started doing near-field in graduate school, everybody said, "This will never work"; "It breaks Abbe's Law"; "What you're doing is clearly a violation of the laws of physics so why are you wasting your time on this?" I would explain about evanescent fields and so forth, and they don't listen. Even by the time I got out of Cornell, people were like, "Eh, what's the big deal?" But then once I started having all these hits—first single-molecule imaging, imaging single excitons, quantum wells, world record high-density data storage, blah-blah-blah-blah, all of a sudden, boom, it becomes a big field, all by itself. It's just like STM. It just took off. Fweeeoo!

Well, you get all sorts of people—people who switch fields to new fields just because something looks hot generally speaking aren't the best scientists or else they would stay in the thing that they were doing and would have thought that was the thing to do. They don't know anything about optics or microscopy or stuff, so they publish a bunch of crap. I felt that every good paper that we published was just justification for 100 pieces of crap that followed in its wake. The signal of the field stayed constant and the noise went to infinity so the SNR went to zero. Everything I was doing was a net negative to society because taxpayer money was funding all that crap work. It was a waste of time and a waste of taxpayers' money. I created the opposite outcome of what I was trying to achieve, which was a positive impact to society. I felt like it was having a negative impact. As the leader of that field, I felt like I was perpetuating that. So, all of those reasons were reasons why even though I had no idea what I wanted to do next, I was 100 percent certain it wasn't going to be near-field.

ZIERLER: Did you have parting words with Harald in a way that you thought you would reconnect in the future?

BETZIG: We kept connected. Not super tight, but tight enough. I was in Murray Hill, still, for a year or two after that. We would still play tennis and stuff. I didn't really go in the building much, I didn't talk much to other people or Horst or anybody, but Harald I stayed connected. It wasn't like I was locked out of the building or anything either, but it was just part of my past at that point. I would hear from Harald about—I would kind of feel vindicated a little bit as I kept hearing about how they kept pushing him into areas he didn't want to go.

Career Pause

ZIERLER: For that year or year and a half, were you on leave? Were you unemployed?

BETZIG: I was unemployed and a househusband. Our first daughter was born in 1993. 1994 is when I left. The idea for the general concept of PALM I had in Murray Hill walking my daughter in a stroller. I published that idea unemployed myself as New Millennium Research, LLC. I figure anybody with an LLC is probably unemployed [laughs] and using that as their cover. That was one of the two papers the Committee cited for giving me the Prize, that one I got while pushing the daughter. It was basically a combination of the spectroscopy experiment Harald and I did plus the single-molecule experiment I did on my own. That was the genesis of the concept.

ZIERLER: Obviously the parallel to Liepmann telling you to take a break—clearly you needed to do this again.

BETZIG: Exactly correct. It was the best thing I ever did. And it wasn't the last time I did it either. There's the time with Harald after I left my dad's company, unemployed again, and that's when we actually did the PALM. We got the last missing piece with photoactivated fluorescent proteins and then we did the experiment, and then that was the second paper the Nobel Committee cited. So, yes.

ZIERLER: Leaving Bell Labs not having a job in hand, were you most focused just on your mental health? Were you concerned that you might not be able to reenter the field?

BETZIG: I was certainly concerned about that. I always knew that I could go work for my dad's company, so I had that as a safety net. That's ultimately what I ended up doing. At that time, I was known. I could have gotten an academic job, probably a tenured academic job, because I basically created that field, but I had no interest [laughs] in an academic job. I guess I could have worked with the guys at IBM. They would have taken me. I had many other contacts because of applications. I knew people in the data storage industry. I knew people in pharma. My range of contacts had broadened substantially. But nothing presented itself as something that I was really interested in doing at that time. My wife was working, we had some money coming in, and I had money saved because I'm a fairly conservative guy in that regard. I just figured I had a window to try to figure things out.

A Stroller and a Big Idea

ZIERLER: You're pushing the stroller and you have this idea.

BETZIG: Mmhmm, yeah.

ZIERLER: What's the idea?

BETZIG: The idea is, again, two experiments that came together. The first one was that with near-field microscopy, I had the ability for the first time to see single fluorescent molecules. It was really because I was getting rid of all of the background signal that exists in the diffraction-limited spot around a molecule and just see the molecule itself. That's what I could do with near-field. I figured if I can see a molecule, okay, fine. But I didn't just see the molecule; I studied its shape, and based on its shape I could statistically tell to even a fraction of the size it looked in the near-field microscope where it actually was. A fraction of the size of the spot that I—if it were a round spot, I can point to the center of the round spot with much better precision than the diameter of that spot. It's just based on the photon statistics I have in the spot itself. Localization of a single molecule, that's concept number one.

Concept number two was, when Harald and I did that quantum well experiment we learned that the excitons collapse and emit a photon not anywhere inside of this nominally uniform sandwich quantum well, but instead at only discrete points. Those discrete points are basically where there is single atomic layer change in the thickness of the quantum well, so the quantum confinement is different. Therefore they get trapped there like in a pothole, so to speak. Then when their lifetime is done they collapse, emit the photon. But also because all of these potholes have slightly different quantum confinement, that means the wavelength of the photon that they give off is slightly different, which you can tell if you're cold, like two Kelvin. A 100-nanometer near-field tip might have 20 of these glowing spots underneath them. Normally you can't resolve, even with near-field, those 20 glowing spots, but because they're all glowing in slightly different colors, if you build up now an x, y, and color three-dimensional space, they are isolated from one another in that third dimension. Now you have three-dimensional balls in that three-space, and now, because they are isolated from one another, I can point to the center of each of those balls, the spatial coordinates. Then I can project that back down the x-y space and basically determine to a fraction of the wavelength the location of every exciton recombination site. If I could do that with fluorescent molecules, then I've got myself a super-resolution microscope that I can run in the far field. That's the idea. That's what I published.

At the time, the only way one could possibly do that was by doing it near absolute zero where the linewidths get narrow enough to do that, and it would have been a real hero experiment, and it's not live imaging at near absolute zero. That's why I just published the idea and tossed it out there and left it, because I didn't know how to make this work easily and at room temperature so you could do live.

ZIERLER: Absent the affiliation to Bell, absent the access to all of the infrastructure, is this a theoretical paper?

BETZIG: Yes, it's a theoretical paper, called "Proposed Method for Molecular Optical Imaging.". Yeah, it was just a theoretical paper with then some calculations on how narrow the linewidths would have to be and the tradeoffs between the density of molecules in the sample and the level of isolation that you would need. So, yes.

ZIERLER: Are you communicating this to Harald? Is he contributing at all at this point?

BETZIG: Oh, yeah. He didn't really contribute per se, but I talked the idea a bit over with him, yeah.

ZIERLER: Did you intuit at all what a big deal this paper was?

BETZIG: Not at the time. I liked the idea and I was thinking about patenting it, but I didn't. I didn't quite go over that bar. Again, it was missing a piece because the only way it could work would be cold at that time. It was nine tenths of the answer but it wasn't the whole answer. We sweated bullets to do that low-temperature near-field experiment we did. It was a lot of work. I couldn't see that ever being broadly applied [laughs] by other labs anywhere. We were really good at what we did, but man, there aren't many people like us, so there aren't going to be that many people able to do that.

ZIERLER: What considerations did you give on where to publish?

BETZIG: I tried to do Phys Rev Letters, which was the star journal at the time, but it didn't even go out for review. It was eventually published in Optics Letters.

ZIERLER: What were some of the referee comments? Do you remember?

BETZIG: Juts like, "Yeah, kind of interesting." I also had another idea which I published in the same paper, which people actually did much later on but hasn't been as useful, which was if you put an electric field on a probe, the electric field drops off in a sharp gradient away from it. You get this gradient. Then the idea is we'd do like MRI but with Stark shift in these molecules. The frequency of emission of the molecules will change under the local electric field that exists. If you have a gradient of electric field, you can position where the molecule is based on its color, based on where it is in that gradient of electric field. That was also an idea that was in that paper. I published it, and shortly thereafter I was working for my dad.

ZIERLER: Was your intention in publishing a theoretical paper that ultimately you would get back to this to run the experiment, or did you just share it with the world?

BETZIG: I wanted to spit on the ground, so to speak, lay a marker that maybe I would come back to, maybe not. Maybe somebody else would do it. Maybe somebody else would win a Nobel Prize. Who knows? But at least spit on the ground with it. That's what it was. It was trying to stake a claim a little bit of that idea. But it wasn't something that I felt at the time was really worth pursuing.

Going Back to Ann Arbor

ZIERLER: Tell me about the family decision to move back to Ann Arbor.

BETZIG: It was pretty much that or really having to soul-search. In addition to all the negatives I told you about why I left Bell, another reason I left—I still wanted to do something impactful. When I went into Bell, I felt very insecure. When I went to Caltech, I felt insecure. Then I did fine at Caltech. I didn't feel insecure at Cornell but I did fine at Cornell. I went into Bell Labs feeling very insecure because of its history, and I did great at Bell Labs. So, at this time—"Okay, so I took some time off! I'm still damn good!" [laughs] Furthermore, I followed my dad throughout his entire career, and I've followed the auto industry and the Big Three. They had ups and downs from the late 1970s onward. Boom, bust, boom, bust, buh-buh-buh. But gradually an erosion—dj-dj-dj-dj-dj-dj—and more and more inroads by Japanese and others into this. On trips back home I'd see what they do and I'd say, "I'm an engineer! [laughs] I think I can do things here that would make this better." I was naïve, okay, but I really felt like I could make an impact, and basically, to put it bluntly, save the Rust Belt. Basically do what Elon Musk actually did with Tesla. I can't say how impressed I am with being able to make an electric car company that makes a profit. They're the first freakin car company in a hundred years that's still around and making a profit! That's crazy! Forget SpaceX, which is even crazier. That guy is a God as far as I'm concerned. But that was my aspiration, was to be able to make manufacturing processes that would allow the Big Three to kick the Japanese in the butt and basically dominate manufacturing. So, I had big ambitions. [laughs]

ZIERLER: We should go back and establish some historical context, the origins of the Ann Arbor Machine Company. What were they?

BETZIG: I told you my dad was a wrestling coach. Then when my sister, his first child, was born in 1953, he needed to make more money than a coach does, so he started as a junior draftsman in a machine tool company. That business, their job is to make custom machines that make one part for a class of cars—a brake caliper, an intake manifold, or whatever. Considering the volumes that they make cars, that machine has to make a million parts a year. That's every 30 seconds, 24/7, with no breakdowns, a million parts per year. The machine is designed around one part, and it will be as big as a house, or the footprint is as big as the footprint as a house, with lots of different stations running in parallel to do different operations. I wanted to see if there was a way of improving the efficiency of that process. Now, my dad worked his way up, eventually became the president of a machine tool company. When the founder died, the founder's son took over. My dad was less enamored of the founder's son, whereas the founder was very much a mentor to him. So, he left and started a competing machine tool company. That was in 1984 or 1985.

As it turned out, there was a very deep recession in 1982 that you're probably not old enough to remember too much of it, but very deep, probably the worst we've had except for 2008 which was short. Then, the Boomers were starting to buy minivans, and so it became a boom time for the Big Three. He caught that wave at the absolute perfect time. His company grew by the mid 1990s to have $70 million in sales and 300 employees. He wanted me to come work for him. Every year, every day. Since in my time off I didn't have any better thoughts, I said—and I do like living in Michigan—I said, "Yeah, sure, I'll come out there and I'll work there."

I started working for him. It was an experience. I learned a lot that eventually became very helpful at Janelia and so forth in terms of how to design for manufacture. Many, many things. But I definitely didn't fit for two reasons. I had two strikes against me by A, being the boss's son, so people figured there's favoritism there. The other strike is that I'm some egghead, right, so I don't fit in for that reason. Most of these guys are just high school educated. But they're making, even in the 1990s, six-figure incomes, because they work their asses off. The other thing that definitely comes from my dad is a belief in hard work. Hard work trumps all. Those guys worked very hard. I worked very hard.

I worked on a couple projects there. The first was a vision inspection system to look at the quality of the parts coming off the machine. Until that time, they could only inspect like every thousandth part and try to statistically determine whether things were coming out to print or not. I used a vision system to inspect every feature of every part. The way it worked was it would do subpixel location of the features using the same algorithms that I used for the single-molecule localization that would eventually be used in PALM, but I was using it for figuring out the location of these things. It worked well and we put it on a couple machines. It went into the field—and they turned it off. They turned it off because it starts rejecting parts. What I learned from that experience is they want to make parts. Now, if the parts bolt together that's good enough. It doesn't have to be within print; it has to be good enough. And they generally over-spec the print by a ridiculous amount. So that was a failure. I said, "Okay, well, if the goal of this business is to increase productivity and inspection decreases productivity, what can I do to increase productivity?"

I learned about what kind of actuators were used to move the machines back and forth and to move the spindles and the tools to the part. There was a big divide. In the old days, they used hydraulics because it was very robust. Again, these machines can't break down. Eventually, electric systems became robust enough that they had largely taken over. They would use big rotary motors with a ball screw to move things forward and stuff. I figured I knew enough control theory by that time that there were ways of making hydraulics more accurate than electrics, which nobody had yet done in that business. There's huge advantages to hydraulics, because if you make a three-axis machine tool, you have one stage, then a perpendicular stage, then a third stage all mounted on top of one another, and then the drill that goes in the part. It's like a rocket, a three-stage rocket, to do a three-axis machining center. Just like in rockets, the more powerful the fuel, the more everything shrinks. If the weight of the top stage goes down, the weight of the middle stage can go down, and the weight of the bottom stage goes down. It's a virtuous cycle.

I found out ways of doing advanced servo hydraulics to make a machine tool that was—the other thing that happens when it shrinks is you have less material, so you have less cost. You have more horsepower because a hydraulic motor, 100 horse fits in the palm of your mind. An electric motor, 100 horse is this big, much more massive. Because the whole machine gets smaller as a result, the Young's modulus materials are the same as it always was, but by being smaller it's stiffer, then. That means it can make more aggressive cuts. You can move to the part faster, you can make aggressive cuts faster. I made this machine that we called Flexible Adaptive Servohydraulic Technology, or FAST. It would move four tons of a three-axis CNC at eight g's of acceleration and position to a precision of five microns. It would move anywhere within about a meter cubed volume in 100 milliseconds. It was like a butterfly or a hummingbird—boop-boop-boop-boop, boop.

I loved that machine. I thought it was great. It was flexible enough to adapt to all sorts of different parts. When one part job was done, when one carline was dead, they could reconfigure that stuff to use on a new job. I spent four years building it and three years trying to sell it, and we ended up selling two of them, even with my dad's best help. My dad was one of the best salesmen I've ever met. It was just way too different for the time and for that audience. People were literally scared of that machine. If you stayed outside of the guarding, everything is fine, but yeah, it was kind of scary to watch [laughs] tons of stuff just flingin around [laughs] like crazy. It was too different. I was trying to sell different to a business that's risk averse. They weren't desperate enough to take on that level of risk. Again, that was a lesson learned.

That was the hardest part of my entire life, because this was my last plan about what to do for my career, and it was evaporating in front of my eyes. The first time at Bell, I felt like I had good reasons for leaving. I knew I had hit physical limits with near-field. With my dad's thing, I never knew, if I kept selling for one year would I have had a breakthrough? There was never that sort of clear, obvious "it's time to quit" kind of thing. It was tough, really tough. In the end, I just did everything I knew how to do to try to get that machine sold, and it was not happening. So, it was time to—again, I'm an asshole. My dad was a far, far better people person than I will ever be. This is why he became such a good boss for people. But that father-son dynamic, you can bet there was a lot of friction because of just the whole father-son thing.

ZIERLER: You mentioned at the outset of today's conversation that there's scientist, there's engineer, and inventor is really the one that resonates with you the most. Was it during your time at Ann Arbor that you most fully felt like an inventor?

BETZIG: Sure, absolutely. I would say with near-field I felt like an inventor. By near-field, I was patenting stuff. I patented some stuff at my dad's company. I felt from that time that I was an inventor, yes.

ZIERLER: But you weren't nearly as application driven at Bell as you were in Ann Arbor.

BETZIG: That's true, but I could foresee enough applications to patent things. I still do consider myself an inventor first and foremost. In fact, Harald and I are going to be inducted into the National Inventors Hall of Fame next month.

ZIERLER: Oh, wow! With the FAST technology, do you feel like you were tapping into parts of your brain that you hadn't really used before?

BETZIG: Yeah, definitely much more of the engineering stuff that I felt like I was good at but hadn't really had a time to focus on because I was focused on the larger picture of the science I want to do with the microscopes. Here I could really focus on the engineering side of it. I just learned a ton about how engineers do engineering as opposed to how physicists do engineering in terms of design for manufacture, how you find the right suppliers, how you document things for being able to fix things later, how you do supply chains, how you do all of that crap. All of that stuff really paid off at Janelia. At the time it felt like I had wasted six years in my dad's company, but after the fact, with enough vision in the background, it's clear that it was time well spent.

Enjoying Blue Collar Engineering

ZIERLER: As an egghead among all these blue-collar guys, looking back what was the value of that for you?

BETZIG: I got to know the guys pretty well. The real impact for me is something later, which still bothers me a lot. Did I tell you the story about Kokomo, Indiana, last time? No? Okay. When I had that vision station, one of the service calls I had to make was to a Chrysler transmission plant in Kokomo, Indiana. When I went there to work on the machine, I went into their thing—it was August. There's no air conditioning. It's all closed. There's grinding machines, there's milling machines, so there's coolant mist, fine metal particles in the air. Sounds from subsonic to supersonic at decibels up to 120 decibels in every frequency you can imagine. Hot as hell, humid as hell because of the coolant.

There are many millions of people in this country who work in jobs of that difficulty every day. Then I end up going to Janelia. [laughs] When I was in my dad's company, you have to worry about every penny you spend. Money is the ultimate metric by which everything is judged. I did six years sitting on a World War II surplus stool where the Naugahyde cover ripped and the jute padding underneath was poking me in the butt, because it was good enough. It didn't matter. The first thing that happened at Janelia when I was a group leader was at the end of a meeting, they took us in the other room and they showed us six ultra plush executive chairs and they asked us, "Which one do you want in your office?" I'm like—you know. Trust me, the people at Janelia got really used to that kind of opulence in a hurry, to the point that you become very entitled. Furthermore, I start going to conferences again. Can academics have an international conference in Kokomo, Indiana? Fuck no!

ZIERLER: [laughs]

BETZIG: It's got to be in Crete! And you've got to go out, and you're eating lobster! And what are they saying? They're saying, "Those stupid rubes in the flyover states that are voting for Trump"—and blah blah blah blah. It's the most immoral thing in the world to me, because it is those people in that plant in Kokomo, Indiana, who are paying the taxes to allow them to eat their fucking lobster in Crete. To this day I have a real antipathy for most academics, because they do not know how privileged they are to be in the position they are. They're so entitled. It's worse than the worst of The Hunger Games. It really sickens me.

ZIERLER: I now have a newfound appreciation of how it's so difficult for you to be a Berkeley professor. [laughs]

BETZIG: No shit! Right? Yeah.

ZIERLER: Just a thought experiment—if the FAST technology was widely adopted, if it wasn't two but it was two million, what would the industry have looked like? What would the impact have been?

BETZIG: It's hard to say. I think it could have had a serious impact on the way machining is still done today. I really do. In the end the technology would have been usurped by further gains in electric motor technology and linear electric motors. At that time, the reason you couldn't use an electric motor to go as fast as we did was because you had to have a rotary motor that would turn a screw to move the stage. At the masses we had and the accelerations we had, the screw would just strip itself completely. Now they have motors that are linear. They're not round. They have magnets in the stages themselves. They had that at the time but the technology wasn't ready for it. It wasn't ready for prime time for another 10 to 15 years, I'd say. So, there was a window of opportunity for the hydraulics. Again, I follow Starship all the time. The first couple flights used hydraulics for the gimbaling of the engines, but now they're all using electrics on it, in the end. So, there was a window for servo hydraulics, but I think things would have evolved in a way that we could have pivoted as the technology became mature to do the electrics. We would have also had much experience about the architectures and so forth that are enabled by having higher power-to-weight ratios. We could have had a market-leading position in that for a long time.

ZIERLER: Of course the Japanese automotive industry continues in the 1990s to eat Detroit's lunch. Is this part of the story, the inability of FAST to make an impact?

BETZIG: I have a lot to blame because I couldn't sell well, but I didn't have a receptive audience. Furthermore, the Big Three in many ways have dug their own grave over the years. Another example is that Kokomo, Indiana, plant trip. At the end of that day, I've worked a 14-hour shift fixing my thing, and it's now about midnight, and I go out to my car—and being the idiot that I am, I drove to a Chrysler plant in a Ford car.

ZIERLER: [laughs]

BETZIG: Not a Japanese car. I wasn't that stupid, okay? But I was in the parking lot in a Ford car. I came out, and it was 120 degrees that day; somebody spilled their entire lunchtime chili all over my windshield, and it had caked on and dried on. I had to scrape that off before I could drive to the hotel at midnight. Anytime I wanted to service my machine inside of that plant, I had to wait three hours to get some big—some UAW guy to bless the fact that I could hold a screwdriver in order to do it. The UAW is nothing but garbage as—look, I believe unions are necessary, but the UAW is as corrupt and as lazy and as such a pile of shit as you can imagine. They are also the union for the postdocs and graduate students here at the University of Berkeley! Unions are absolutely essential but they can go too far, and trust me, in the auto industry, they went way too far. They still go too far.

But they have lots of votes. This is why you'll see Joe Biden have an EV ensemble talking about EVs and he doesn't invite Tesla. Why? Because they're not unionized. That's why. So, the Big Three dug their own grave. Every time they get into trouble—2008, GM went bankrupt, right? Ford had to mortgage everything they had to keep from bankruptcy. Chrysler has been bought and sold more times than I can count anymore as it has gone through one set of suits after another. But they are all slowly dwindling like an ice cube in hot water. They got smaller and less relevant every year because they rely on the government to try to fix their problems rather than fixing their problems themselves. It's just the way it is.

ZIERLER: It was time for you to get back to the science, is what it sounds like.

BETZIG: I guess so! That's right. And I decided I missed science, so that's right.

ZIERLER: I think that's a perfect narrative break point for next time. We'll pick up with Janelia Farms in 2002.

BETZIG: Oh, we're going to do a third round?

[End of Recording]

ZIERLER: This is David Zierler, Director of the Caltech Heritage Project. It is Monday, May 20, 2024. It is my great pleasure to be here once again with Professor Eric Betzig. Eric, it is great to be with you as always. Thank you so much.

BETZIG: Thanks, David. Nice to talk to you again.

ZIERLER: Eric, today we are going to pick up with your return to academia. By way of introduction, I wonder if you have perspective on the origin story of Janelia Research Campus.

BETZIG: Yeah, a little bit. It was really spearheaded by Gerry Rubin, who was a fly geneticist. He worked at Carnegie Institution and then Cal. While at Cal he got interested in, as a runup to trying to figure out the human genome, to do the fly genome. He ran into lots of bureaucratic roadblocks at Cal to do a project on that scale, so he walked up the hill to LBL. There, Chuck Shank was the director of LBL at the time. He said, "Cool," and offered him space and resources. The rest is history. They were able to do that in short order and get that.

ZIERLER: Was LBL's supercomputer relevant at this stage?

BETZIG: Not so much. It was more just having a good, cordoned-off, large space where they could set up all the stuff they needed to do the sequencing. Chuck had the space and thought the idea was worth pursuing, and that's all it took. I can't speak for Gerry, but I have a feeling that that episode heavily influenced the way he wanted to set up Janelia and run Janelia. The idea to minimize bureaucracy—because one of the things Gerry said later was that, having been at Cal, he designed the administrative structure at Janelia to be the anti-Berkeley, to minimize red tape as much as possible. Just as Chuck acted in sort of a dictatorial capacity to make this happen, Gerry was the benevolent dictator who ultimately ran Janelia.

Janelia Farms and Return to Academia

ZIERLER: Where did you first meet Gerry?

BETZIG: That year, 2005, it's like I was blessed. A lot of things just fell into place. Within less than six months, both the work that led to my Prize plus Janelia all fell into place. After I left my dad's company, I was trying to develop some kind of intellectual capital, since I hadn't written a paper in ten years, to get academia to listen to me again and try to find a lab to do some science. I came up with this idea for a vast multifocal excitation field through optical lattices to do fast 3D imaging, inspired by when I first heard about green fluorescent protein. Again I was a decade late to that party. The way I contacted Gerry was, in order to try to get somebody to listen to me to do that idea on the optical lattice, I called in all sorts of bets of people I knew at different institutions. One of the people I contacted was Horst Störmer, who was my boss at Bell and who had gone to Columbia. He said, "It sounds like a cool idea, but if you want to do biology with it, don't give a talk in the physics department; give a talk in biology."

He hooked me up with Rafa Yuste, who had been a postdoc of Winfried Denk's at Bell. Rafa invited me to give a talk in Biology at Columbia. At that talk, one of the people I wanted to speak to, who I already treated as a God, was Marty Chalfie, because he was one of the guys behind the GFP. After the talk I was with Marty in a cab going to dinner—and Rafa and I think Mike Sheetz—and Marty said, "Well, that's—" I mean, the talk was so theoretical. There's no way any biologist would understand. But at the end, I said it would be this much faster, this much less invasive, this much better resolution than confocal, duh-duh-duh-duh. He understood that much anyway, and he said, "That was interesting, but how are you going to implement it?"

Just the week before in Physics Today there was a little article that described something I had never heard of called the Howard Hughes Medical Institute. There was some crazy guy I never heard of called Gerry Rubin who said he was going to set up a biological Bell Labs. I said to Marty, "I don't know. I'm still pretty averse to academia but this is something I believe in and want to do. I saw in Physics Today just recently that there was some guy wanting to create a biological Bell Labs for something called Howard Hughes Medical Institute." Obviously Marty knows all about all of that, and he said, "Well, maybe after you've proved yourself out a little bit, maybe that would be suitable." I kind of figured that was the end of that. Then two weeks later, I get a call from Gerry Rubin who said, "I saw Marty Chalfie at a party and I heard that you might be interested in Janelia." [laughs] I said, "Yeah. Definitely." So, I went to Janelia. Northern Virginia was a different place at that time. It has completely transformed as the government has continued to grow, and contractors, and it became the center of 80 percent of the internet traffic, and it's filled with large faceless data centers. At that time it was vineyards and horse farms out there. I flew into IAD and then driving on this little road up to Janelia. The building was still just a steel frame. The pond out in front was a big mud pit.

I met Gerry. It was the most amazing experience, because so many times when Harald and I—at this time, Harald and I had gotten back together and were talking about ways of getting back into science, and we just kept bemoaning how if we were kings of the world, how we would do things differently and we would set it up differently. I started talking to Gerry, and Gerry was on exactly the same wavelength and had exactly the same thoughts. He was building Janelia to try to recreate a Bell Labs-type culture. I just couldn't believe how much we were in sync on things to do. We hit it off immediately. I got one of the first group leader positions, even though I had been out of science for ten years, because Gerry could do what he wanted. He was the dictator of this thing, and he thought I'd be worth a try.

I went from rags to riches instantly once that happened. The building wasn't going to be ready for another year but they gave me a budget, so I rented out some space in Michigan where I was still living and started to do some initial experiments. From the beginning I kept saying, "You've got to hire this guy, Harald Hess" I'll get back to the PALM story and how that relates—within weeks of that same time the PALM also fell in my lap—but we were taking the PALM microscope after we'd built it in Harald's living room to NIH to do the experiment and Jennifer Lippincott-Schwartz's lab. It's small so it fit inside a suitcase. [laughs] One of the early group leader meetings was in progress at the time—and Chuck Shank, who Gerry of course decided to get as an advisor, as a senior fellow and one of his senior advisors as he's putting Janelia together because now they had a relationship from the drosophila thing—Harold opens up this suitcase, and I could just see in Chuck's eyes that immediately—yeah, they gotta hire that guy. [laughs] Harald was pretty soon on the payroll as well. That's how I met Gerry. Gerry was great for years and years.

ZIERLER: Did Gerry have a preexisting relationship with HHMI?

BETZIG: Oh, yeah. He has been an HHMI investigator since like the 1980s. In fact he moved up the ranks so that by the time of the drosophila project or shortly thereafter, he was actually a VP of HHMI. He was right up there going to the trustee meetings and all the rest. He held a lot of sway at that time and was able to pull this off.

ZIERLER: Did he envision microscopy to be a major component of Janelia?

BETZIG: They did. Well before I got involved, around two thousand—basically the legend goes that he and Tom Cech, who was the president of HHMI in the late 1990s at the time, sketched out the idea when Gerry was bemoaning to Tom about what would be needed to recreate a Bell Labs for biology. They decided to put on a series of workshops through HHMI to figure out what are the unmet needs in biological science that they could address. They came up with two areas. One was understanding the principles behind neural computation, neural circuits. The other was to develop new imaging technologies, specifically microscopy for biology. That all happened [laughs] even before I contacted Gerry. It was really the stars aligning, because Harald's and my interests and background were absolutely perfect for what was already one of their stated goals.

ZIERLER: The Bell Labs concept for biology, how did that translate in terms of the focus either on fundamental research or applied research?

BETZIG: I don't think there was any thought about what is the difference between pure and applied research. Gerry says he viewed Janelia as a social experiment. The idea is, could we replicate the idea of small labs where the PI is at the bench, where he is funded well enough that he doesn't have to worry about grants or anything else? The idea is to get the PI at the bench doing the work himself, and in order to do that, to really limit group size. And conversely, have a lot of shared resources to take a lot of grunt work of cloning and other stuff that would otherwise require a large group in order to do. That was inspired by Bell, and also the Laboratory for Molecular Biology at Cambridge in the 1950s. He was a grad student of Sydney Brenner.

ZIERLER: Oh, wow.

BETZIG: He knew from Sydney the whole history of the LMB and how they—it's a small world, David! [laughs]

The Magic of Green Fluorescence

ZIERLER: This is Shangri-la. This is exactly how you want to get back into science, academic science.

BETZIG: Yeah, but it's amazing these little connections where things percolate. [laughs]

ZIERLER: This idea that with green fluorescence, you're ten years late to the party—I wonder if you've ever reflected on the benefits of that, of not having preconceived notions of what was going on.

BETZIG: I've often reflected on the wasted years because I didn't pay attention to it when it came out.

ZIERLER: But obviously this was good, given what happened.

BETZIG: Chalfie's paper came out one year after I left Bell Labs. I had pretty much felt like I had met a dead end in trying to do live-cell imaging by super-resolution. If I had stayed, there's a chance that it would have led to PALM five, six, seven years earlier. We didn't have photoactivation yet, but photoactivation in dyes was a thing with Tim Mitchison and so forth. If I had kept in that area and focused on that, it might have happened. It is also possible I would have developed something like lattice light-sheet earlier. It's hard to say. At the same time, there were benefits for working with my dad. I learned a lot of techniques that I wouldn't have had otherwise. Who the hell knows what all these alternative histories would have led to? [laughs]

ZIERLER: All right, so you get to Janelia. How do you set up your lab?

BETZIG: Again, luck. When I was still trying to find a home for my optical lattice, I gave a talk, thanks to Steve Chu. Again, it's a small world. He was at Bell, and I knew Steve from that. He was running LBL at that time. I told him I was trying to get a job. He said, "Come to Berkeley and give a talk." I gave a talk about my optical lattice there. At the end, a graduate student by the name of Hari Shroff approached me and said, "Wow, that sounds really cool." I said, "Great, I'm looking for post…" At that time, I wasn't looking for postdocs, but as soon as the Bell thing was up, then I contacted Hari again. Also, a little bit later somebody told another grad student looking for a job—Na Ji, also at Berkeley—about my idea, and so she contacted me. I hired both Hari and Na, and they were my first two postdocs. They were both from Berkeley. They were both absolutely fantastic. The three of us together just hauled ass. For a long time, for the first few years, it was just the three of us—Na working on adaptive optics and Hari working on PALM. Man, we just cooked! We worked insane hours again like I did in the Harold days, and just, yeah, immediately took off.

ZIERLER: What were the big research questions? What were you pursuing from the get-go?

BETZIG: Again, it was within a week or two after the trip to Columbia that as part of that same sort of roadshow to try to find somebody interested—Harald had had this connection to the Magnet Lab at Florida State. There we met Mike Davidson and he told us about photoactivation. Then we dropped the lattice idea like a hot potato and we immediately jumped into the PALM. PALM was a race. It's so easy everybody can do it, and everybody was on our heels. We were lucky to put our noses across the finish line first.

ZIERLER: When you say, "so easy," why was it so easy?

BETZIG: Because all you need is a wide-field microscope and a couple lasers and you have super-resolution. You can build it in your living room. This is the definition of easy! [laughs] It was ripe and ready to happen once photoactivation—particularly given that I had that theory paper that I had published in my early unemployed days after Bell about how you could do super-resolution by molecular isolation and localization. All you needed was a good means—the localization was easy; the isolation was hard. But once photoactivation came on the scene, it was obvious that the problem was solved, that the key was in the lock, and this was it. Hari worked like hell towards doing initial live cell imaging with PALM and so forth, to extend what Harald and I had done with Jennifer in the fixed, dead cell work. Super-resolution was a race at that time in terms of who can do what when, first.

ZIERLER: How were you keeping tabs on the race? Who else was involved?

BETZIG: Who were the competitors?

ZIERLER: Yeah.

BETZIG: Stefan Hell, who shared the prize. Xiaowei Zhuang, who was doing something similar that she called STORM, at Harvard. W. Moerner at Stanford. Stefan and W.E. shared the Prize with me. There were many others. Dozens, literally. I gave a talk actually even before we submitted our paper, which was dumb, in I think November 2005. Again, it came out of this whole "I'm trying to find a job" thing. I contacted everybody I could think of to get help finding a job. Dave Piston—a microscopist, biologist—was able to wrangle me an invitation to this conference at NIH in November on biological imaging and microscopy. We had almost all of our data by then. This is still 2005. I presented that data. It was before we even submitted our paper, which is in retrospect not a wise idea.

ZIERLER: [laughs]

BETZIG: Everybody was pretty much aghast. It was like dropping a bomb in that room. It was a big room filled with everybody who is anybody in biological imaging, and it was—yeah.

ZIERLER: What was the data telling you and how did you convey it?

BETZIG: Telling us that yes, you can get 10- to 20-nanometer resolution in cells, and non-invasively. This was revolutionary. And that you have protein-specific contrast of the things you want to see. Fluorescence was already a big deal because of that protein-specific contrast. To have that now at the near-molecular level with the promise of potentially getting to the molecular level, and the promise of being able to do it in live cells, and being able to do it on any microscope that exists anywhere in the world, this was a big deal! [laughs] That was a big deal.

ZIERLER: We've covered before but we should go into a little bit more detail now—why is live-cell imaging so important? What can you do as a result?

BETZIG: This is my current hobby horse and something that I've been working very hard to convey to people, is that animation is what defines life. In the twentieth century, the real wins for techniques in biology were molecular biology, structural biology, and biochemistry. They're so effective that most biologists think nearly completely in terms of those three paradigms. But they are all exceptionally reductionist approaches, by taking the cell and grinding it into its pieces and then looking at certain parts. There are 20,000 different proteins, tens of thousands of metabolites, lipids, everything else. When you just focus on one or two things at a time and you focus on it in a static manner, as those techniques do, you don't even know all the things that you're missing. You don't have the right stoichiometry. You don't have the right partners together. It's amazing we know anything, honestly! [laughs]

Deeper Than a Moving Image

ZIERLER: Is it almost like the difference between a photograph and a movie in their ability to tell a story?

BETZIG: It's much deeper than that. At least in the photograph, you have a picture of all the things and you can try to extrapolate in your mind what the movie is. Imagine the photograph in which 99.9 percent of the pixels have been blown out because you don't know what all the missing pieces are. That's where we're at. That's what it's like. And then trying to understand the dynamics on top of that? It's bad enough if you have just the still photograph. And, no prior knowledge—even if you had a still photograph of a dog running, you have enough priors in your head to guesstimate what the motion would be. There are so many things in biology where those motions, you have no priors. That hasn't stopped biologists from actually creating animations and movies of things happening. They're all cartoons, complete cartoons that have very little to do with the reality of what is happening.

The inside of the cell is stochastic. Everything is happening starting at the molecular level under Brownian motion guided by differential coefficients for interactions with other things they bump into! Us talking, everything—is due to that! It's emergence from that! You cannot understand that by breaking cells down to their parts. It's just like trying to understand a car engine from a random pile of engine parts. That is damn hard to reverse engineer. Again and again, your mind is going to go and you're going to hypothesize certain things that eventually get translated into belief as fact when they're just hypotheses that are 99 percent of the time probably wrong or highly incomplete! The only way you're going to understand a complex dynamic system is by looking at it being dynamic. That's it! It's obvious to me! It has been obvious to me since I got frustrated with PALM, that this is the way forward. That's my rant!

ZIERLER: Have you been surprised that crystallography remains a favored observational technique?

BETZIG: No, and crystallography has actually kind of taken a back seat to cryoEM, right? Because you don't need to be able to crystallize. And now AlphaFold, to be able to use the cryoEM data to then predict other protein structures. But again, people don't realize how limited those approaches are, because in order to get a cryoEM or a crystallography image or a diffraction pattern or any of that requires putting the protein in one state, one low-energy conformation state, and that's what you image. Proteins wiggle around like this all the time in the real environment! They adopt many conformations! All the stuff being done with cryoEM, crystallography, AlphaFold, it's fine, but people don't realize exactly what a limited set of the actual conformations these things form that they're actually seeing! They're missing the dynamics completely!

An example of that was something again we learned through doing the live-cell PALM which led to Eikon Therapeutics, which was that an important part of many proteins is they have certain regions on those proteins that don't fold into a certain conformation. They're intrinsically disordered. In order to do crystallography, you can't get the thing to crystallize unless you strip off those intrinsically disordered regions, so you never see them. If you do it by cryoEM, you're doing particle averaging, and those disordered regions are different in every particle so you don't see them! [laughs] It turns out those intrinsically disordered regions can be key for how proteins interact with one another. The only way to see all that stuff is to look in the live cell at how the protein kinetics actually work in reality! That's what led to Eikon. It's possible to do that thanks to PALM! [laughs]

ZIERLER: In the history of science, we connect Brownian motion—it's part of Einstein's miracle year in 1905. Has Brownian motion gained acceptance in biology for its importance at this point?

BETZIG: The biophysicists understand it. Biophysicists understand, and at a certain level understand certain things like patterning during development or other processes in terms of gradients and stochasticity and so forth. But their models are so simple that I'm sure that they too are just missing 90 percent of the puzzle. Again, in academia it's just you have certain communities who have parts of the puzzle, and other parts of the puzzle, they sort of are aware of one another but they don't really interact and talk to one another in any significant way most of the time.

ZIERLER: The idea that you can take this technology and it could work with any microscope, I wonder if you can talk about standardization and what that actually looks like.

BETZIG: You get your own cells. You get these plasmids that you transfect the cells with to express the protein. You can put it on any wide-field microscope that has a decent high numerical aperture objective like you would use for doing any kind of fluorescence imaging in cells. You turn on one laser, a purple laser that photoactivate the molecules. You turn that down to a low intensity and a few spots come on. You record an image. You wait for those to turn off, turn on another. Shine the green light to light up those molecules. Take image after image of sparse dots. Put that into a computer, find the centers of the dots. Start building up another image that is nothing more than the locations of all the dots distilled from all of those individual sparse images of dots. Pretty soon you've determined to nanometer resolution the location of every fluorescent molecule and thus every protein of the one you were interested in within the sample. As long as you have a decent optical microscope with a decent objective, the magic is all on the biology side. The magic isn't on the microscopy. And the software to localize this stuff is pretty damn trivial. Any grad student can write that in a week.

NIH and the Race of Discovery

ZIERLER: You share this data at NIH. Is it understood at this point that you've won the race, or do you realize, oh my God, I've got to write this paper first?

BETZIG: It was obvious to me we won the race. However that was not obvious to some of our competitors. Let's just put it that way.

ZIERLER: What were the differing perspectives or biases?

BETZIG: None, really. It's just a question of who talks the loudest, pretty much. We were at a considerable disadvantage because we had no support. Others had bigger support behind them.

ZIERLER: You mean like Harvard, Berkeley, institutional support?

BETZIG: Harvard, Berkeley, Stanford, Max Planck, blah-blah-blah-blah. We were the outsiders, right? I still consider it a miracle in the end that I shared the Prize. It's to my everlasting disappointment that Harald didn't share it too, but they can only give it to three. The three they picked were certainly deserving, but Harald was deserving as well.

ZIERLER: This data is out there in the world. What happens now? How does this change your own research?

BETZIG: It certainly continued to put fire under us to get that paper out. I thought that paper was going to be a slam dunk. I thought we'd submit it, it would be accepted in a week, and published the week after. I was naïve about that.

ZIERLER: Where did you consider publishing?

BETZIG: Science. This was clearly going to be—I totally agree with everybody's bitches about Science, Cell, Nature as having too much of a monopoly over publication and the negative consequences that come with that and all of that. At the same time, if you're a technologist who is developing tools for biologists, if you publish your paper in a technical journal, nobody is going to see it! If you want to find collaborators, Science or Nature or Cell is the place to publish! [laughs] Still to this day. They haven't fixed that problem. It's better with bioRxiv and with other things now that didn't exist then, but yeah, so Science is where we sent it. We first sent that—I can't remember when. Was it April 2006, something like that? We wanted to dot a lot of i's and cross a lot of t's. We could have submitted it much earlier but we really wanted to get a really solid, solid thing. Then came back the reviews. Two were like, "Oh my God, I can't believe this." Then you always have the—reviewer number three. [laughs] Reviewer number three said, "I don't believe a word of this and I won't believe a word of it until you can show correlative electron microscopy with super-resolution." Do you know how hard that is? It is—we did it. We did it in about a month and a half.

ZIERLER: Explain why it's so hard first.

BETZIG: Because the protocols that are involved in staining things for electron microscopy will kill any fluorescent thing you want to look at. Plus you have to do registration. You have to find out where you imaged, what you imaged, be able to somehow correlate that to the contrast you have in an electron microscope. You're trying to find the exact same tiny field of view to see by EM afterwards. It's a real bitch. Harold and I finally published a definitive paper on that in 2020, but that initial effort was exceptionally difficult. Exceptionally difficult. We did it. It cost us some more months. Then we sent it back. "Here you go!" They sent it back to reviewer number three, and reviewer number three says, "I still don't believe it. I don't think this should be published. This is garbage." So they sent it out to reviewer number four. Reviewer number four says, "Are you guys being idiots? Why haven't you published this?" [laughs] Then it was published.

ZIERLER: Do you think that third review improved the paper, going back and having to do that?

BETZIG: Not enough for the effort that was required. I don't think the main message of the paper or anything else would have been any different. Now, I totally believe in the value of review, and God knows I've had many papers that have been improved by review, but having that EM was not necessary to get to an understanding that the resolution gains were real.

ZIERLER: The data doesn't become more bulletproof as a result of this complaint?

BETZIG: It becomes a little more bulletproof, but I don't honestly think that there's anybody who felt like this was artifactual in any way even without that. It was clear in that talk I gave that everybody believed it. It was obvious that it would work. It was obvious that it did work, even without the EM. Once you have the idea in your head, if you're in the field, it's like, "Yeah." It's a slam dunk.

A Worldwide Enabling Technology

ZIERLER: Did you realize the significance of this being an enabling technology that people all over the world would take it and run with it in ways that you might not even envision?

BETZIG: Yeah, I did. That was my hope. In fact, in my opinion I felt too optimistic, because I feel like super-resolution in the end has not really had much of an impact other than Eikon and the single-molecule tracking stuff in live cells. I don't think any of the structural stuff has had a significant impact at all. It has led to a gigantic community of lots and lots of papers, lots of people, lots of conferences, but again they're looking at structures and things that have been known by EM or other means for years and years and years. There's little hits here and there, but for the amount of effort that has gone in it hasn't moved the needle at all. That frustration was what drove me towards live-cell imaging. I just didn't feel like this sort of—resolution alone is not enough. As a microscopist, you're in it because you're thinking of resolution, but that metric is often not even the most important metric.

ZIERLER: Are you starting to get calls from academic departments? Are you happy at Janelia for the time being?

BETZIG: I didn't really get many calls from academic departments. In fact, did I get any? I don't think so. I was very happy at Janelia. I kept pinching myself as to how did I get back into something that's like Bell Labs? It was better than Bell Labs. Harold and I lived on campus. Hari and Na lived on campus. We just worked and worked and worked. Janelia is a country club for scientists. Bell was a little scrappy. The resources were a bit limited. Not terribly, but facilities were a bit old. They had a lot of history and that was great. And great, great people, fantastic people. But Janelia was like shiny, new, and just lavish with budgets and with everything. There was no reason to leave. [laughs] Particularly considering I've always hated academia. [laughs]

ZIERLER: Is this registering with biotech yet? Are people thinking about this value for therapies and drugs?

BETZIG: I think there was a little interest in that. I didn't really push in that direction. It wasn't really until Robert Tijan became president of HHMI. He pushed us into doing this transcription imaging, and then that led to Eikon. That really opened my eyes to that world and what would be possible there.

ZIERLER: Did you stay with this work after the paper came out, or did you branch off in new directions?

BETZIG: Oh, yeah. Again, it was a gold rush, like I said, those years. The paper was published in 2006. Our first talk was 2005. By 2008, it was—pkoo!—everywhere. Zillions of people doing this stuff. Zillions. By 2009, that's when I was done. I was thoroughly done with it. Part of that was because I understood the limitations. There's many other limitations than just most of the time you're looking at fixed and dead cells. The length of the linker that you use to attach the fluorophore to your protein reduces the resolution. There's non-specific labeling of the protein. There's—duh-duh-duh-duh-duh. I can go on and on and on, but there's all sorts of practical problems that limit you.

At the same time, I was living the same nightmare over again that I had with near-field. When I finally got near-field to work well, a huge field spread up around it, and all these papers were published, and 99 percent of them were just crap. The same thing was happening with PALM all over again, just crap-crap-crap-crap-crap. I said, "I've done it again. I've created a giant bandwagon where there's a lot of taxpayer money being funded that's a net negative in the end to society because of that waste of time and resources." That was my attitude. I loved it for several years—I lived it—but when I found its flaws, it was time to kick that girlfriend to the curb! [laughs] And look for a new direction.

ZIERLER: Tell me about the flaws. What were you seeing? What was surprising to you?

BETZIG: In any microscope, the image you see is a very imperfect representation of the original specimen. The more work you have to do to process your specimen for your microscope, the worse of a representation it is. I think of it like a sausage factory, where the real thing goes in and some distorted thing comes out that you image. There's a black box sausage factory in the middle. Because you have to do thousands and thousands of images of all these molecules and find their coordinates, that takes time, and so it's slow, so it's not really conducive to fast live imaging where you want to get a complete picture of morphologies by having every molecule figured out. So, it's super slow, so it's not great for live imaging there. Single molecules require high photon doses, which is also bad for cells, because they will die or be sick under the light illumination. Chemical fixation—if you fix it, in order to have the time to pull out every molecule's coordinates at your leisure—those fixations disturb the ultrastructure you're trying to see. EM people have known that for 50 years! Over and over and over again, you'd see these papers coming out where people are doing chemical fixation, which I know is ruining the ultrastructure, and then coming up with insights that are nothing but artifacts that they're seeing in their images.

Then, non-specific labeling. It is not a problem when you use fluorescent proteins, but if you bring in dyes that can photoswitch instead, which became very popular—because they're brighter than fluorescent proteins—they can go to anything. They can stick to anything. They don't necessarily have to stick to the proteins you want. So, you're seeing all these things light up that you think is structure but it's not. It's just non-specific labeling of other stuff. We don't need to go on. I could give an hour talk about all the limitations. And I have, many times. Most of it falls on deaf ears! If you're interested and if you have the time, at the end of February I gave a talk at Janelia. It's on YouTube. It's called Confessions of a Frustrated Optical Microscopist. It's an hour-long rant which will go through all of this, and why we're doing what we're doing today.

ZIERLER: But that's the story in a nutshell?

BETZIG: That's the story in a nutshell.

ZIERLER: You mentioned initially the software was trivial. Did it remain as such, or with higher and higher resolution do you eventually have a big data problem on your hands?

BETZIG: With PALM, not so much. We have a big data problem on our hands today and it's by far our most limiting thing, but it's not PALM. The nice thing about PALM is in the end, all you need is to know the coordinates of the molecules. You're going from images that are many megabytes down to, for each image of spare molecules, a few kilobytes of data. It's super compressible. Once you got into 3D, there was a little more work to do there, but generally speaking, compared to most problems in data science and biology, PALM never really had any real limits.

The Nobel Buzz

ZIERLER: When does the Nobel buzz start? When is it too hard not to pay attention?

BETZIG: I'd say around 2008 it started. It was a pain. I just tried to tune as much of it out as I could. I was largely successful. I just focused on doing other stuff. The Nobel thing could have gone any way they wanted. Who the fuck knows who they'd pick or whether they'd pick it at all? Even to this day, I still am not sure that this thing justifies a Nobel Prize. I think if Eikon can discover things with it, I might change my mind, but as of today I would say that this was a mistake, that it really doesn't deserve that level of recognition.

ZIERLER: This is relative to discoveries that happened around it other years? What are you basing it on?

BETZIG: There's always things that are really impactful out there that many people don't know about. In my year, for example, the one that won the Physics Prize was the blue LED. That was a super inspired decision! When I learned the story of Shuji Nakamura and how he was on this godforsaken small island in Japan working for Nichia and coming up with all of this virtually singlehandedly—and it basically reduced energy consumption in many places by ten percent! There hasn't been a more impactful thing to reduce carbon since! And it's everywhere. It's ubiquitous. There was so much physics that had to be done in order to make the blue LED work, and he did it all himself. There are stories like that all over the place, where people are doing super, super, super impactful stuff compared to what we've done. The only argument you can make for ours is that it beat a law of physics. But anybody who understands enough physics knows that it didn't beat a law of physics. All it's doing is exploiting a loophole, a different loophole than near-field exploited. Near-field was exploiting the near-field loophole, and PALM was just basically exploiting the loophole that, yes, you can't resolve two things, but you can certainly find their location if you have prior knowledge they're isolated to much less than the wavelength. That's it!

ZIERLER: You're emphasizing impact as a criterion of the Nobel Prize, but lots of Nobel Prizes are given purely for theoretical discoveries.

BETZIG: Sure, but come on! [laughs] This is pretty trivial! [laughs] It's not like I'm coming up with quantum electrodynamics here, okay? [laughs]

ZIERLER: All right, all right. But still, it's still a fun story—where were you when you got the call?

BETZIG: I was in Germany. I was getting ready to give a keynote at a conference in Munich. I was sitting in the office of my host because I was there early. He had gone out and then my cell phone rang. I wasn't thinking about what day it was and what week it was which is the Nobel week, at all. I was just focused that I'm here to give this talk. But as soon as I saw that it was a European number before I even clicked send or okay or whatever, I just immediately went, "Oh, shit." [laughs] My first reaction—again, they have this guy call you right after they call to get your first impressions, so that's also on YouTube—I said to him my impression was equal measures of happiness and fear. That was really accurate. Happiness that if it was going to get an award I was probably going to be reasonably—if it got an award and I wasn't part of it, I was probably going to be somewhat bitter. Thank God Harald is not. He's a far better man than I am.

The fear was that at this time, I had shifted over to the live imaging. I was in that office working on the proofs for a lattice light-sheet paper. I have never been more proud of any paper in my career than that paper. We were just on such a momentum with that technology, and that paper was such a beautiful paper. I love that paper! Half of the shit on this wall is from that paper! I was remarried, had two young kids, Janelia is going great, and all of a sudden I know this thing is going to just impact my life. It really felt like getting hit by a bus, just one of those events that you have no way to foresee, you don't know what's going to happen, and boom, you're just in shock, and you're like, "Shit. Everything has been going so good, and I know that this is going to be a zoo." I thought for a few seconds about declining it. Then I remembered from Feynman's book he talked about—he first heard from a newspaper reporter. He talked with the newspaper reporter about declining it. The guy said, "If you decline it, you're going to get so much more attention than if you accept it." Then I thought about my family, my father and everybody else and how they'd be disappointed if I—so I didn't even—all of those thoughts went through my head probably at warp speed in ten seconds, and then I accepted my fate. [laughs]

ZIERLER: Do you think from Stockholm's perspective it was a coin flip whether to give it to you or Harald?

BETZIG: Probably not. The one differentiating thing is, first off I had more history in super-resolution with near-field. The other thing—I don't know if others found it important, but I found it important—was the principle of PALM I published when unemployed, based on the quantum well experiment I did with Harald and the single-molecule localization experiment I did with near-field. I published basically the concept of PALM in 1995, in Optics Letters, or I can't remember where the hell it was. It is really laid out there. The only thing is, what is the means by which you're going to isolate all of those molecules when there are many in one diffraction-limited area? At the time the only way I knew back in 1995 was like we did with Harald, and if they glow in different colors you can isolate them spectrally. But once we heard about photoactivation, you could realize you can isolate them temporally. That was it. If they had to give it to one of the two of us, I think I was the more logical one to give it to, but Harald took just as big a risk as I did. He passes the deletion test with flying colors. There's no way I would have done it, no way it would have come out anywhere near as good. All of that. He deserves it just as much as I. But looking from the Committee's point of view and this three-body problem that they have, I guess I can understand their decision.

ZIERLER: How did you deal with all of the pomp and pageantry in Stockholm?

BETZIG: It's fine. It is kind of weird. It's still weird, but that week was particularly weird. They really run you ragged for that week. They give you a driver and a car, and they plan your schedule all day long every day for the week. You go to all sorts of places, talk to all sorts of students. Had to go into a chemistry lab and pretend I knew any chemistry while the students were doing titrations and so forth. [laughs] It was fine. It's a strange zoo. Some of the pressure was off—a funny story—they give you this black limousine with a driver, and at the end of the day you come back to the Grand Hôtel and you get out of the car. Again, because of the blue LED people, all three of them were Japanese. There were tons of Japanese press. Probably dominated all of the rest of the world press combined in this. Every time the black limousine would pull up, Na and I would look out and see all these cameras and all these people focused on the door. As soon as we come out of the door, they'd go, "Aww" [laughs] and drop their cameras. "Hi guys!" [laughs] That gives you a dose of reality again! [laughs]

ZIERLER: An issue all Nobel Prize winners have to deal with—of course the platform it gives you, if you choose to talk about things well beyond your area of expertise. How did you deal with those decisions?

BETZIG: I say no. I can probably count on the fingers of one hand, and I can't remember any examples offhand, in which I've agreed to sign a document that is being signed by others or so forth. I am really cognizant of my limitations. I really feel uncomfortable giving public opinions about things that are not within my area of expertise. People want an opinion about microscopy, I'm the guy to come to. I even pontificate frequently about how I believe science should be done. Not that I think that that has done any good to change the way science is done. All of these other causes and so forth—I remember when I went to Lindau the first year, they were doing some declaration—what the hell was it on? I can't even remember. I think it was climate change or something. I don't know enough about climate change to know how big of a problem it is, if it's existential or not, or what should be done. I'm cognizant very much of whenever there's advocates of anything, they often lose sight of the fact that there are tradeoffs. Everything in life has tradeoffs. If you're just espousing one side and not considering the tradeoffs, I generally am not interested in hearing your opinions because I don't think you've done your homework.

The Lattice Game Changer

ZIERLER: I wonder if your excitement about the lattice work was an anchor to keep you focused amid all of this attention.

BETZIG: It helped for sure. I knew I had something to come to, and I had plenty of unfinished business. There's a fair fraction of scientists who get the Nobel pretty late in their careers, in which case that kind of defines them and that's what they do. They want to travel. They want to do whatever. It's a free ticket to anywhere you want to go on the globe. If you want to visit China or India or wherever, you can make a call or two and pretty soon you're flying business class to wherever just to give an hour talk. It's kind of a golden ticket in that way. But I've got young kids. I've got things to do in science. If anything, I kick myself to this day for how much time I spent in 2015 and 2016 on the road. It really slowed down the inertia we had with lattice, with adaptive optics, with structured illumination, and all of our other work. We kind of got it done. Particularly if I knew that fucking pandemic was coming up, I would have said "no" a lot more often. You first say yes because the requests are coming from people you knew or people you owe in the past. Then if that's near another place that invited you for whatever reason you might do it to just knock off two in one trip or three in one trip or whatever. But yeah, 2015, I called that "living in an aluminum tube." It blows. I gained a lot of weight, ate a lot of meals, didn't exercise. I wish I could have those years back, to be honest.

ZIERLER: Let's go back to the happy place. What was so significant in your mind about the lattice work? How did it change the game?

BETZIG: It was the first tool that could look at life on life's terms, that life is a four-dimensional object—x, y, z, and time. If you want to be able to understand it, not only do you have to have high resolution across all four dimensions of space-time, but you also have to do it with low toxicity so that you're not harming the cell or changing the processes you're trying to study. Lattice solved all of that. We really started around I'd say 2012 just bringing in one group after another as collaborators, outside people into Janelia to work with us a couple weeks, take data. A lot of these were people who had been studying the same systems for 20 years. They're jumping for joy as they're leaving after two weeks because they've been seeing things in these systems they've studied for years that they have a whole new perspective about. There was no doubt that this was game-changing in terms of people's abilities to see and understand systems in biology. That was fantastic.

That 2012 to 2014 period right before the Nobel, it was just awesome. Just awesome. We tried to continue that, but we also wanted to move on, and so then we started an imaging center at Janelia to take the load off of us, so that those kind of collaborations could happen with the lattice light-sheet in this imaging center. Then that became a pretty big thing at Janelia where Harald's volume electron microscope went in, Philipp Keller's developmental biology lattice light-sheet went in, and so forth. It spun off in a good way in the end, and eventually I was able to get back to thinking, before goddamn Berkeley came along and ripped us away.

ZIERLER: Where does adaptive optics fit in here?

BETZIG: You can learn a lot by looking at cells. In fact, the vast majority of what people know about the dynamics of cells is by looking at cells on a cover slip. The reason they do that is because when you look at the cell in an organism, there's enough differences in the refractive index of the nuclei to the cytosol to other organelles that the whole thing is like looking through a bag of marbles when you look through multicellular systems. The only way to get around that is with adaptive optics, to basically measure how the light is getting scrambled by that refractive index variability and correct for it, and then get back to good resolution. The other alternative is to look at cells in cover slips where you don't have all that obscuring other cells that are messing up the light. That's why the vast majority of what we've learned from live cells has been cells in cover slips.

There's two problems. First off, they didn't evolve there, so in order to make it so that they can live on their own, if they're mammalian cells you have to muck with their genetics. You end up creating these Frankenstein monster cell lines like HeLa cells or U2OS or COS cells that are aneuploid. They don't even have the right number of chromosomes. They've been immortalized and changed in other ways to make it so that they're healthy enough to live on the desert that [laughs] is basically a cover slip. So, you don't know that what you're seeing is the reality inside of the organism. The other thing is I've soaked up enough biology to know that the phenotypes you see in your microscope are the result of gene expression, and gene expression is controlled by the environment. If you put a cell in an artificial environment like a cover slip, you're not going to get the right gene expression and the right phenotypes. How can you trust what you see, no matter how good your microscope is? Lattice light-sheet wasn't the end, because we could look at cells that look great on a cover slip but we can't trust the data. We need to look at cells in tissue with lattice. We had to have the adaptive optics. That was the genesis of the adaptive optics lattice light-sheet, which is probably the second proudest paper I have. That came out in 2018 right before we went to Berkeley.

ZIERLER: Is the adaptive optics that you're referring to more or less the same that we see in astronomy like at Keck Telescopes?

BETZIG: It sure is. We ripped them off completely!

ZIERLER: Did you hang out with astronomers? Is that where you learned adaptive optics?

BETZIG: I wanted to be an astronomer when I was at Caltech! [laughs] I've always followed astronomy. I think I said in one of our earlier talks about how I was also inspired by Bill Bridges, because he did this demo of adaptive optics he did in Hughes Research Lab with the Starship Enterprise. That stuck in my mind. Adaptive optics in astronomy—there, they shoot a laser into the stratosphere to excite sodium atoms to make an artificial bright guide star near the thing that they want to see, and the light from both of those things comes in the telescope. You pick off the guide star light which is high SNR, and you put it into this what's called a Shack-Hartmann wavefront sensor to find out what the distortion is based on how that star has been distorted. Then you change the shape of a mirror that your astronomical signal bounces off of, to exactly cancel that distortion and get back to the diffraction limit. Yeah, the Keck Telescopes have that. TMT will have multiple guide stars for multiconjugate adaptive optics. In our case we use a two-photon laser to create a guide-star by fluorescence inside a biological system, image it on a Shack-Hartmann wavefront sensor, change the shape of the mirror. It was exactly the same, yeah.

ZIERLER: It's amazing to think that it's the same technology applied at such different scales.

BETZIG: Well, yeah. [laughs] Another talk that you will find—in fact, I mentioned this before—I think in 2017 for one of the alumni year things at Caltech they asked me to come, and I gave this talk on historical connections between astronomy and microscopy. The take-home message of this talk is that microscopists are the retarded stepchildren of astronomers because we steal everything from them 50 years after they do it first. I actually make a connection between exoplanet discovery and PALM as well in that.

What a Scientist Can Never Know

ZIERLER: Oh, very cool. This is as much a philosophical question, a bias question in science—but the idea, especially with the lattice work, that you're observing the cell in its native state, how do we know that to be true? How do we know that as a result of this technology, this is really what it's like?

BETZIG: You don't. You never do, for sure. In fact, I can give you two still unsolved problems. The first is we're still dependent on fluorescence. When you put a fluorophore on a protein, you've just stuck a 2-kilodalton bowling ball onto that protein. You have to work very hard with the genetics, do lots of control experiments, to make sure that that protein seems to be acting as it normally would without that, but you can't really be sure. That's number one. Number two is cells don't like light. Lattice light-sheet is a big step forward in reducing the amount of dose that cells see when we're imaging them, but it's not zero. Again you try to do experiments where you start with very low intensity and get a vague idea of what's going on, of the dynamics, and then work your way up to an SNR where you get really good data, and hope to see if you're seeing the same kind of dynamics you saw at low intensities. Likewise, when you're done, keep the specimen around and make sure that it's still alive, it still behaves, it still reproduces, it still does all of that. You do what you can, but it's like the Heisenberg principle—if you observe the system, you're going to change the system. It's just the way it is. We've worked really, really hard to minimize that amount of perturbation, but we can never be sure.

ZIERLER: Can you imagine a next-generation technology that removes even this level of perturbation?

BETZIG: I think there will be eventually other things that will help. You can come up with all sorts of science-fictiony ideas. On the one hand, fluorescent proteins are not great fluorophores. In principle, according to theory, one should be able to create a multilevel quantum mechanical atomic-like system that could be interrogated at very narrow wavelengths and get very high SNR, have a cross section that's roughly equal to the wavelength as opposed to the cross-sections that are just a few square angstroms that fluorophores have. That's theoretically possible. In a real environment, when you have all these electrostatic influences of water molecules bouncing around like that, will that ever happen? I don't know. That's one way. The other way is to say, "Screw light," and use something less invasive that can't ionize anything. So—acoustics.

There's a guy, Mickael Tanter in France, who took the PALM idea, and what he did is he created little bubbles of different size, not nanoscale but close to nanoscale bubbles, that are disperse [?] in their sizes. Inject that into the vasculature and use ultrasound to do PALM localization based on resonating with those—those different-sized particles will have different wavelengths at which they will resonate. You can do isolation based on the frequency of absorption of all those different bubbles, so you can get a super-resolution ultrasound image of, for example, the vasculature inside a live organism. Completely noninvasive. Beautiful data, beautiful data. There's a guy working in similar lines at Caltech, Mikhail Shapiro, who is now working to genetically encode little tiny bubbles that the cells themselves, the organisms themselves make, to act as markers to doing imaging by ultrasound of that stuff. Some years of development of that type of thing might lead to us throwing away light altogether and moving to sound as a way.

There's all sorts of ways, with any type of radiation that one could conceive of doing to try to get images of stuff. There's ideas for doing things by—there has been for a long time—in fact my original paper on the PALM idea also suggested using a magnetic field gradient like in MRI to look at then changes in spectra that occur with that as a way of doing it. Or doing it by Stark effect with an electric field. Those ideas could potentially lead to sort of a super-duper resolution MRI type approach that would be noninvasive to do stuff. Again, all of this stuff requires years and years and years of development, but the vague bones of the ideas are there.

ZIERLER: The narrative that you've set up, it's almost comical—you're delighted being at Janelia, it's the research antithesis specifically of Berkeley, and then you getting the call and deciding to accept the offer. How does that come about?

BETZIG: It comes about because of my wife. [laughs] My wife was a graduate student at Berkeley, as I mentioned. Well, she was my postdoc. Na Ji, the second postdoc. Eventually we fell in love and we got married. I knew in those years, sitting around the pub eating dinner with her and Hari, that—for the two of them it was always, "Oh, Berkeley is so great. Oh, this restaurant." That restaurant. The weather. This, that, the other thing. Duh-duh-duh-duh. I knew when I finally married Na that probably my days were numbered. At the same time, I still loved what I was doing at Janelia but I felt like the institution was failing on its promise to become a biological Bell Labs. I was perfectly happy there. I'm still a Senior Fellow there. I still love going there and interacting with people that I interact with. But it is a very different place from when it started.

ZIERLER: Is that about leadership change, about moving away from Gerry?

BETZIG: Yes, it is. Gerry no longer being the leader was one. Gerry himself in my opinion is culpable for part of this, because he didn't adhere to his own principles. As soon as you started to have biologists in the building, they're all complaining, "We can't get anything done with just a lab of six people! We need more people! We need more this! We need more that!" Then eventually there was some pressure about, well, we need people who have some academic experience. So, they bring in some academics, people who have been in academia. They immediately start becoming power centers and trying to change the culture to be more academic. Then the new president of HHMI has a big effort on education, so there's a lot of education-related stuff at Janelia—students all summer, students this, students that, duh-duh-duh-duh. There are so many thousands of places of education in the United States; why do you need to take the one place which focuses on research and making it into a university? Which is effectively what they've been doing. It's just a shame.

All my life I felt like I have watched entropy in action. I grew up in Michigan, watched the decline of—Detroit was the second or third biggest city in the United States when I was born. In n 1960s when I was a kid, it was like L.A.! Now it's nothing. I watched that happen. I watched the auto industry decline. I watched my dad's company eventually get sold and go away. Things just have a lifetime. Bell was a weird counterexample. There was a 60-year period when it was the place. Again, just a few weeks ago I was there to help celebrate Lou Brus's Nobel, the tenth one for the Labs! That's crazy! It just feels like every place has a natural lifespan and decline—this is a 64-year-old man talking, so give it a grain of salt—but I believe in entropy! [laughs] It happens. It takes a lot of energy to create an anti-entropic pocket, but it takes even more energy to maintain the anti-entropic pocket. Eventually dust in the wind, man! [laughs]

ZIERLER: Do you think the Nobel gave the credibility to have your appointment at Berkeley exactly what you want it to be?

BETZIG: I didn't really want it to be anything. Basically I just came along. I negotiated a large startup. I have fairly limited duties compared to most professors in terms of teaching and service and all the rest. I still chafe at all of it. I don't like being here. Everything we try to do in our lab is ten times harder than it would be at Janelia, whether it's placing orders or dealing with floods because of decaying infrastructure, or rooms overheating because of decaying infrastructure, or them just not giving a damn when we want to put in a hundred-gig line and it takes them three years to do it. It's what I expected, given Gerry's rants about Berkeley in the past. And it's academia. I don't resonate with academics. I'm not interested in what they're interested in. A lot of academics, the reason they band together is because there's reasons in terms of getting grants together, shared grants and stuff like that. I've never written a grant in my life to the government. I hope to go to my grave never having written a grant to the government. I consider that the primary source of mediocrity in academia, because of peer review, that in order to get your grants you have to get along with your peers. Pretty soon it's just a bunch of like thinking towards mediocrity. I'm doing the best I can with being here. It helps to have a small connection to Janelia. I feel like while there was some slowdown because of those years after the Nobel, the slowdown between the pandemic and the move to Berkeley has been far worse. I'm trying to pick up momentum again. I'm not well suited to this place; let's put it that way.

ZIERLER: What about LBL? Is that an asset for you?

BETZIG: No. It potentially could be. In fact, I was going to have a joint appointment there, but as soon as I started to read all their IP shit and like that, I said, "I'll wait until I actually need you guys before I sign this stuff." As it turned out, I haven't needed them for anything. With what we're doing now, using the Perlmutter supercomputer could be quite valuable, but there are other AI resources out there that I'm exploring instead.

ZIERLER: This supercomputer, it's named after Saul?

BETZIG: Yes, yes.

ZIERLER: What does it do? What is the purpose of this computer?

BETZIG: Until recently it was like the fifth biggest in the world, but it has like 30,000 GPUs. The big problem today for our work is the analysis of the images from the lattice AO. I've been a huge skeptic about AI but I've come to the conclusion that it is the only way to be able to do the analysis at scale that we need. We've been concepting out what would be required in terms of both the data and the compute, and it's prodigious, probably a bigger AI project than anything happening in the world today.

ZIERLER: This is a statement for just how big the datasets are becoming?

BETZIG: Yes, yes, yes. There's an opportunity in the last few years, as the big players have moved beyond LLMs and into—vision transformers they're called—the architecture to be able to understand images. Most of that stuff is 2D still right now. We're 4D or 5D with our data. The architecture seems to be the right type of architecture for what we want to do, but these newer models are based on transformers. They do self-supervised training of the model based on vast datasets that are unlabeled. Other earlier AI models used annotated data in order to train their thing. It takes a huge amount of human effort or computational effort to annotate large datasets to train an AI. One of the advantages of these newer architectures is it can use unannotated data in order to train. It does self-supervision. But in order to do that, it requires really vast data, so vast that this is a limitation to what a lot of the big players are doing in vision. Who are the people who are better than anybody in generating vast datasets of 4D dynamics of living systems? [laughs]

ZIERLER: This guy. [laughs]

BETZIG: It's potentially a marriage made in heaven, right? That's what we're pushing against right now.

ZIERLER: How did you fare during the pandemic? Did you stay home? Did you still go into work?

BETZIG: I went into work as much as I could. I'd go nuts if I were at home. We did what we could. I actually spent most of my time working on a theory paper for improving optical lattices. I'm pretty proud of that paper. It's very dense, very computationally and theoretically dense. It's not game-changing, compared to the—but it's definitely an improvement on it. Just like my original lattice paper, it is probably going to get about 20 citations despite my [laughs] pride in it. You have to be a real hardcore nerd to dig into that paper. It's probably like 40 pages of equations and then simulations, and then the simulation is backed up by the experiment. It all matches up perfectly.

ZIERLER: To the extent that COVID was an all hands on deck kind of situation in science, did you think about coronaviruses and microscopy?

BETZIG: I wanted to stay as far away from that as possible. My MO usually in things is if people are going in a certain direction, I want to run in the opposite direction. I always want to work in a space where people are not. That was a crowded space.

ZIERLER: Were the technologies that you developed utilized by others?

BETZIG: I don't think so. I don't think that they played any role. I don't know what people might have done with lattice or PALM in terms of corona, but I haven't heard of it having any kind of influence on what happened. Not that it couldn't. Particularly the lattice potentially could, and the lattice AO potentially could, but again, the world is huge, and it still astonishes me how few people know about lattice and lattice AO despite my efforts over the last decade to preach from the hilltops about what they're capable of.

ZIERLER: It almost sounds like you need another Nobel Prize to get attention on this.

BETZIG: Yeah, well, that would definitely kill me! [laughs]

ZIERLER: On that note, let's bring the story right up to the present. What are you working on these days?

BETZIG: Exactly what I was saying. Worked a long time, got to the lattice AO, 2018. First came here, wanted to start an imaging center modeled after the imaging center we did at Janelia. Then the pandemic hits. No visitors then. If you watch that video on YouTube you'll hear a lot about why I think everything we've done so far has been a failure. The fundamental limitation of lattice and lattice AO is that the movies look beautiful, but they take forever and a lot of manual input to make those movies, even though taking the data takes minutes. It can take weeks to generate a pretty movie and months to do analysis on a small dataset. The inability to analyze the data makes these tools generally useless. They have a lot of potential but we have to be able to create a scalable solution to generate biological insights from 4D and 5D live imaging data. While in both the lattice AO paper and a few other papers we used analytical tools to extract biological insights, it has required millions of CPU hours and several man-years of effort for one question. To make it scalable, AI is the answer.

I've been advocating for that now since the beginning of this year, talking about wanting to create a cell observatory. I've always been a guy who has been a benchtop scientist who believes in doing things with his own hands at the bench, but I think that—we worked very hard to get lattice light-sheet in other people's hands, in other labs, more recently with the lattice AO. It has largely been a failure. Again, I explain why in that talk. But even to the extent that they can succeed in replicating these things, they're stuck with the same data problem we are. That's the major bottleneck. None of these technologies, as good as they are, is ever going to have any effect until we can solve the data problem. Ultimately, I didn't think that was possible until these newer transformer-based foundation models came on the scene in the last couple years in AI. They seem really much better attuned to the vision problem than anything that came before, and potentially applicable to us.

But the complexity of the microscopes, the diversity of organisms and things that people want to see that require a lot of genetics and a lot of animal care in order to do—because we're looking at animals and not cells—and then the vast AI resources to build the AI models and then the GPUs needed to then actually run the data and get inferences—it is not a tabletop kind of thing to do. It is not a one-lab thing to do. I'm dragged kicking and screaming to the model of having to have a much bigger institute in order to be able to do that. For me, it's kind of like up until Hubble, people were largely doing astronomy on their own. Herschel had his big-ass thing in his backyard. Hubble had the Hooker Telescope which was supported but largely still at a fairly small effort. At that point, it changed. By the time of the Hale, forget it. Once the Hale Telescope was on, that was the first exemplar of where astronomy was going to be forevermore. It wasn't one guy with one telescope; it was a place where astronomers would come, have time on the instrument, get their data. The same thing with Keck, and going to be with TMT and so forth.

I think that's where this type of biology unfortunately has to head. We need an institute that can first crack the nut of developing an AI model to be able to analyze the data. Because the instruments are so complex and expensive. Because the organism preparation, the husbandry is so expensive. Because the AI is so expensive. We're talking about a cell observatory that you would create where people would then come with problems, biological problems, and it would be looked at with our microscopes and analyzed and present back to them the results. Ultimately that AI model could be queried by anybody. Any data that's like that, people could mine that data for whatever else they want to pull out of that data. That's the vision, and it's me going around—I know zero AI but I've been talking to AI people left and right for the last three months, trying to find people willing to fund this effort. This whole week is nothing but Zoom meetings talking to AI people or funders about trying to get this thing going.

ZIERLER: Given the centrality of AI for where you want to see the research headed, you couldn't be in a better place in terms of the Bay Area.

BETZIG: The Bay Area is certainly a good place to be. I'm trying to play to my strengths of this area as much as I hate living in this area.

ZIERLER: Do you think AI is the thing that might make you say it was all worth it to come to Berkeley in the end?

BETZIG: Sure. Yeah, yeah, yeah. I'm trying to make lemonades from my lemons. [laughs]

The Centrality of Hard Work

ZIERLER: There you go! I want to hear where all of this is going. For the last part of our talk, just a few retrospective questions. I'm always interested in the Caltech alumnus perspective. What has stayed with you from your Caltech days, the way that you define what it means to be a scientist?

BETZIG: The value of hard work is number one. There are very few times I worked as hard as I did at Caltech. It instilled in me a belief in the value of hard work. I think that has paid off in spades. I think any success I've had in my career is because I work harder than most people. Creativity comes from hard work. You have to be able to completely devote yourself to the task. When you do so, then your subconscious mind is starved from thinking about anything except the problem. The answers come when you're in the shower or waking up in the middle of the night, or when you're in the middle of a job or whatever as to, "Why didn't I think of this?" But it requires the hard work to prime the subconscious and to keep any extraneous thoughts that it would think about away. Hard work is number one of what I got at Caltech.

ZIERLER: Was it also as an undergraduate where you learned to minimize the distinctions that we make in our minds between chemistry and biology and physics? That it's all just science?

BETZIG: I don't think I've ever been thinking in those siloed ways either before Caltech or after. What else have I gotten from the Caltech experience? Definitely some humility. There were plenty of people out there way smarter than I was. That became obvious at Caltech. That has stayed with me. I'm grateful for the few professors and so forth who have had a lasting impression on me. However, on the other side, it was really a distorting experience. The Caltech of today I think is very different from the Caltech then. It was a meat grinder, for sure. It definitely led me to an understanding of my limitations that I didn't appreciate before, and an understanding that everybody must have limitations as well. Hard work is really important and you really want to push, but you have to have compassion when people reach their limit. So I think there's that. I'm still not sure that I wouldn't have been better off—again, you can't turn the clock of time back, but I do kind of regret that I didn't become a more well-rounded person until far later in life, with a lot of bumps along the road. It's interesting, I haven't kept up with many people from that time. It feels a little bit like with the fellow people—sort of like you're veterans of some really nasty war. You'd just as soon not dwell on the battles and the blood.

ZIERLER: A lot of PTSD there.

BETZIG: Yeah, yeah. I hope it's a bit different now. The first time I went back to Caltech since I graduated was when they invited me for this Distinguished Alumnus Award. That was 2015, 2016. I graduated in 1982. I had no real desire to go back [laughs] to the place of those battles. Now I've been back a few times, and it's just almost unrecognizable compared to what it was. It was funny—I was reading a couple weeks ago—I was thinking about Bill Bridges again and I was reading some Caltech oral history thing that he had done. He specifically referred to the period when I was there as a time when they were making big mistakes in admissions because they weren't doing well enough to pick people who could take what Caltech had to offer, so to speak. He said how he was talking to somebody in the health services department who was explaining all the problems that the undergraduates were having and how this was a problem.

ZIERLER: From your perspective, the miracle of Bell Labs, how did it work? Do you have any hope—Janelia tried, maybe that's an open experiment—do you have any hope that that model will ever see the light of day again in the United States?

BETZIG: You can never say never. Janelia succeeded for a little while. I'd like to believe if I can build this cell observatory I would try to create such an environment, although I don't intend to stick with it for more than about five years. There were unique things about the Bell thing. Of course the monopoly, which gave them all the funding they needed. It turned out communications was an incredibly diverse question that required expertise from an amazing range of physical sciences and engineering to address well. I've said this before, and I'll get in trouble for saying it again—there was a lot of value to the old system in which men worked and wives stayed at home. Then you can really kick ass, if you have that support at home. It has its costs, right? It has its costs to ambitions of women. It worked very well for the men who were at Bell who were working really, really hard. It would be hard—whether it's male or female, working at that level and having a family, it's not easy. I work as hard as I can, but I have the family. I know that I'm not as efficient and not as good a scientist as I would be if I were working like I did when I was at Bell, but that's the tradeoff that I want to make. I'm lucky being remarried that I have more time with my second set of kids than I had with the first, which was largely while I was—when I was unemployed it wasn't a problem, but once I went to Janelia it was a problem. So, I'm not sure that you could recreate it.

I also think, speaking a little more philosophically, that the generation—the halcyon days of Bell Labs from right at the end of the War up through to probably the 1980s or 1990s, that generation of people who were in charge were adults. They went through World War II. Many of them went through the Depression. They know that things are not always cushy. They understood that it requires hard work. It requires effort to keep that entropy at bay. I think that the vast majority of Americans today don't have that knowledge of what has created the world that we live in, the prosperity and freedom we have, and how simple it would be to lose it all, and how we're slowly letting ourselves lose it over time. That sort of entitlement is corrosive, and it will require a similarly negative event of the scale of World War II to refresh in people's minds what's important—what's important in terms of family, in terms of creating a collaborative mutually supportive society that can move forward and extend on what people behind us have done.

ZIERLER: I know you don't hold yourself up as any kind of other model for other people to use for their own scientific careers, but given how you checked out of academia and then came back in such a big way, what are the lessons? For people that are not feeling it in academia—I don't know if inspiration is the right word, but what are the words of strength that you might give where people should follow their heart and do what they want to do regardless?

BETZIG: I'm asked that quite frequently by people who run across my story. That's exactly what I say is to follow your heart, and to remember that the world is so vast. Particularly academics, the nature of the system just puts blinders after blinders on top of you. You work towards getting a PhD, then you work towards tenure and so forth. Your world contracts into this narrow discipline that you're working in and so forth. I think with wistfulness about all of the potential careers I think I could have had and just never had a chance to do. I had a pilot's license when I was in high school. I think I would have enjoyed being an airline pilot. Every time I go on a plane I wish I were up in the cockpit to have their view instead of my crappy little view I get out of the window that I got. I would have liked to have been a cook. I would have liked to have been a park ranger with the National Park Service. There's all sorts of alternative things where I think I could have had a really fulfilling and enjoyable life. I don't look at a risk taken in one thing as like the end of the world. People are so risk averse. I'm glad I got that from my dad, this ability to take risks. People overestimate the downside of the risk and completely underestimate the potential upsides. Even if there are several false starts when you're picking yourself up after a failure, there's always—and damn, those failures, they teach you. [laughs] You learn a lot from them. I feel sorry for people who just follow in one little tried and true path for their entire career. They're missing so much! We have so little time on Earth. So little time, so little opportunity to have any influence. To waste it away is just sad. Really sad.

ZIERLER: If you measured the Nobel Prize based on the impact that the Nobel Prize should recognize—the technology that you've developed, where is the world simply not ready for this, where we might see these things be embraced 20 or 30 years down the line? Is it AI? Is that the linchpin here?

BETZIG: AI has the potential, yeah. It also scares me too in terms of its misuse. I don't mean necessarily malevolent AI for the AI sake. I think humans driving it in malevolent—which is already happening, right? We're getting more and more to the point where you simply cannot believe what you see [laughs] anymore. I can't believe a video. I can't believe an image. I can't believe that there's actually a human behind this or not. Those days are gone. I don't know if AI is the big potential source. Did we ever talk on the topic of energy in all of our—?

ZIERLER: A little bit, yeah.

BETZIG: A little bit. I'm really interested in that topic. If I can't get the cell observatory going or it doesn't work out—energy is the defining problem of the twenty-first century. I'm convinced of it. It isn't just about climate change. It's about prosperity for the parts of the world that have been left behind. That's a billion-plus people who have been left behind. If we want to bring everybody up to our standard of living, we need to develop vastly more energy resources than we have today and do it in a sustainable way for the ecosystem. There's no question if I had more years in me and I wasn't focusing on this, that would be the area I would go into. I'm hopeful that already just the natural course of human invention has given us a long lease. Natural gas has saved our ass, no question about it. We emit less CO2 pollution because we're burning methane instead of coal and oil, with higher Carnot efficiency. Nuclear is clearly the final answer, but there's still a lot of work to be done in that area. The world is always going to be filled with many problems for many scientists and engineers to figure out. AI will be some part of that. It may become even a great tool. I was falling asleep like a week ago and I couldn't sleep and I turned on an old Columbo episode. Are you old enough to know Columbo?

ZIERLER: I know of Columbo, yes.

BETZIG: This is in the 1970s, and they have a scene in an office. I'm looking at what the people are doing and the typewriters and all of this stuff, and I'm like, my God, that world is gone, just gone. The telephones. It just—how vastly different the world is from 50 years ago. Not just AI but solutions on energy, everything else, the world 50 years from now is going to be so unrecognizable to the way it is now, in some ways bad but I'm still hopeful that in many ways good, because of people bustin ass to make it better. To make it better as scientists, as engineers, as creative people as musicians, as whatever. There's just tons of opportunity for us to continue to improve. I'm hopeful for my kids that that's the way it will work out.

ZIERLER: That's great. We'll end on that and we'll continue on that optimistic note. Given your focus on the cell observatory, best case scenario, for the five-year timeline that you're giving yourself and if everything works out within those five years, beyond that five years what does that look like? What do you hope to accomplish?

BETZIG: What I hope to accomplish is to be able to take everything that anybody can do right now in terms of cell biology that is done on a cover slip, and he able to get those insights in an organism, anywhere in the organism, any developmental stage. What that would mean, for example, is right now when people develop drugs, they develop a drug, they test it first on cells, they test it in people. They have no real knowledge of how it's delivered, what are the off-target effects to any other part of the organism. If we could for example create some organisms where we get a baseline of information of how dynamics and how structure and how cells are working in a healthy state, and you start to apply drug candidates to these organisms, and you look across the whole organism with AI, and you say, "Did this compound have any effect other than the positive effect it has on the one thing you're interested in? Did it have negative consequences elsewhere?"—that kind of thing. There would be just a million questions that we could answer almost immediately through the AI.

Again ultimately it would have a large language model around it where you would interrogate these—any question that you have, that any biologist had through history, about—what is the mitochondria's role in digestion? [laughs]—all of those questions could be asked in that way and the model could start presenting data to you to do that. I really think this would unlock imaging from being sort of an also-ran in biology to being as transformative as those years in the LMB were to put molecular biology as to a major player in biology. I think imaging would become a major player if you had the ability to access all of these things. It would get us closer to ultimately being able to reverse-engineer the cell to the point of possibly creating a cell in the end. There's a lot of ways this could go both practically and fundamentally. I look at all the things that people study and by far the greatest level of mystery is, this is the most complicated matter we know in the universe, and we know so little about it. There's so much mystery inside of here. Damn, if I were a physicist, this is the system I would study. We know neutron stars far better than we know anything about our own cells. Isn't that crazy?

ZIERLER: What a wild idea. And one to keep you invigorated for some time to come.

BETZIG: Yeah!

ZIERLER: Eric, I want to thank you so much for spending this time with me. It has been terrific.

BETZIG: Sure thing, David. It has been very nice talking to you.

[END]