Eric F. Wieschaus

Interview

Interview, March 2009

Interview with the 1995 Nobel Laureate in Physiology or Medicine, Eric F. Wieschaus, 17 March 2009. The interviewer is Adam Smith, Editor-in-Chief of Nobelprize.org.

Eric Wieschaus discusses the appeal of doing research in the lab, the value of giving youth opportunities outside their normal experience (11:57), the importance of selecting a research question that is both fascinating and difficult to answer (21:10), the reasons why his collaboration with Christiane Nüsslein-Volhard was successful (30:38), the heterogeneity of scientists (51:40), and the risks of calculating career choices based on averages (57:55).

Interview transcript

Eric F. Wieschaus: The mixed feeling about being at a place because you’re a Nobel Laureate, meaning being carted in because you’re on display and it doesn’t really have that quality quite, but you would much more like appreciative people wanting to talk with you because you had something interesting to say, or they heard about your experiment from last week or something like that, rather than because you have a tag as a Nobel Laureate. In part, it’s always this conflict, because I guess you understand that it’s valuable for the public to have people, scientists, to be successful, designated as having been successful. These become potentially role models for young people, so there is a value in the award and in the recognition, but it is still a strange thing to be among the few Nobel Laureates that are out there.

You seem to have almost consciously avoided the changes that can come with laureate status.

Eric F. Wieschaus: Yes. If your life is okay, if your life is successful. I lived in the lab, I do stuff, I do experiments actively at the bench myself. At the time when I received the award I did that, I worked five or six hours a day, still at the bench. I teach, I have a family. I don’t have much more time in my life, but the way my time is spent is pretty good for me. I’m happy that way, so why would I want to change things? I was curious, I had very few active decisions, thoughtful decisions, after receiving the prize, but one of them really was this conscious choice that I would not be a Nobel Laureate, in an odd sense.

We came back from Stockholm and I didn’t know what to do with all the stuff. We went to the local bank and we never had this, but we had a little bank box thing. We rented one of those boxes with keys, a deposit box, put all that stuff in it, in 1995, and I haven’t seen it since. It’s there someplace, and I think we still have the key, God, I hope we have the key. It’s there, but … Because I like the way things were before.

I imagine the prize gives a certain sense of security, and yet you didn’t need that really, I suppose, in the first place.

Eric F. Wieschaus: I think it’s a nice thing that people recognise what you do and recognise the value of what you do. It also brings a certain power, not real power, but in the sense of a certain ability to influence or your opinions matter. Newspapers sometimes will call you up. Or if people want you to participate, if you go to a local high school science fair and you walk around and talk to people it brings them pleasure because of who you are. But …

There’s a danger in that as well.

Eric F. Wieschaus: Yes. The reality is that from a personal gratification standpoint, everyone who’s received a Nobel Prize has already has that to some degree. You don’t get a Nobel Prize out of the blue because suddenly the Swedes figure out that you did a cool experiment that nobody else has recognized. Reality is that by the time I received the award, the experiments were already highly regarded and people understood their impact and understood that they were important. I had as much recognition as any scientist would really want to have in their life. The Nobel Prize is something that’s really an important thing in my life, and it did give me security. It did give me a certain sense of position in the world that I didn’t fully appreciate, but it is a nice thing to have happened, but it would be very sad if it were a necessary part of my life. I suppose that’s what my choice was, the absolute belief that this thing was not necessary.

One hears of people who don’t receive the prize, who seem to have been concerned with the idea of winning it and that must be a burden.

Eric F. Wieschaus: Yes, that would be sad because like all things, it’s a /- – -/.

We’re sitting here on a beautiful spring day in Princeton, which has been your home for what, 28 years?

Eric F. Wieschaus: Something like that, yes.

Obviously it suits you. What is it about the place that’s so right?

Eric F. Wieschaus: It’s a small town, a great university, great students, wonderful opportunity to do science. I am happy with the size, the department that I’m in has maybe 35 people, 35 scientists, all of whom I respect and all of whom I interact with. We teach together, we work together. There is a strong sense of intellectual community that’s satisfying for me here. It’s an easy town to live in. I have a family, my wife is also a professor in this department. We don’t collaborate or do science together, but it’s because we’re both living in this small town, we are able to manage our lives and get things done. Get home in time to throw a dinner together for the kids, all of those things that made our earlier lives, when we were a little bit younger and in developing our careers, a lot easier just simply because we could have a family here and we could do our science in a fully committed way. And that worked out really well for us.

Does the smallness of the department and indeed of the small-town feel contribute to your ability to stay in science? Because one of the unusual things about you is that you still do several hours bench work a day.

Eric F. Wieschaus: I think it clearly does. If I had to commute 40 minutes from a house into the laboratory, my life would be more complicated, I wouldn’t be able to do science. When our children were at home either my wife or I would come back into the lab almost in the evening after we finally got the kids to bed, from nine to nine to one or something like that and get us an extra four hours in, because we live 5-10 minutes by bike, away from the lab. You can hop on the bike and get in and all those things make it easier. I just found it an easy place for me to figure out what it was. It was small enough that I could control it. There weren’t that many variables. At lab I have teaching. I have my university responsibilities administratively, but all those things were kind of definable. I could say, I could do this and this and this, and I could manage. If things were bigger, maybe if there were more opportunities, maybe things would’ve been different, but I felt comfortable with being able to manage things here.

It’s actually quite a rare talent to be able to be able to manage the opportunities and not to get drawn away into all the administration and the kind of empire building and stuff. That must be a temptation?

Eric F. Wieschaus: Ah, noted. No, no. I got into the business because I like doing science. I like being in the lab. I have this crazy sense that every time I’m doing an experiment it’s as exciting as the experiment that I did yesterday. I know that’s not true. I know that I’ve had great experiments and good experiments, but any experiment when I’m doing it, at the time that I’m doing it, seems like it’s going to be a great experiment. There is no attraction to me beyond, other than doing science. I like teaching actually and the reason to be good teacher, but I’m conscious of the cost because teaching means that you have to organize yourself, get up, give formal lectures for an hour and an hour and a half. It costs to do, for you to be a teacher, and that’s a different kind of cost. When I go into the lab, it’s like the totally natural thing for me to do. I plot down in front of a microscope and start sorting flies or checking expression patterns or thinking about things or designing crosses. That’s natural. It’s the only thing that I do that doesn’t take any effort at all ever.

What a blessing.

Eric F. Wieschaus: Yes, absolutely.

Did it come naturally? Was that when you were growing up, were you a scientist as a child, do you think?

Eric F. Wieschaus: Perhaps, I don’t know. You look back and you try to figure out who you were as a child. My family are not scientists, they’re not academics. I grew up in Alabama, in Birmingham in the 1950s and 1960s. I didn’t know that people could be scientists. My father worked in the steel industry and then he and my mother eventually had a construction company and they built things. I didn’t know the possibilities. I wanted to be an artist. I painted, I drew, there’s a part of my character that’s very driven towards visual things that even plays into my science heavily. I know that in part, me being an artist was the same part of me that eventually became and me becoming a scientist. Fortunate for me was that I had certain chance things. I was able to go to a summer science program when I was in high school and actually left Birmingham, Alabama and took a train to Lawrence, Kansas to the University of Kansas and lived there for a summer when I was like 16 or 17. For me, it was wonderful, that nerdy little high school kid, and then suddenly going off to Kansas and living in a dormitory with, I suppose, other nerdy little high school kids. It was suddenly a social situation that was different than the so typical social situation.

When you’re a young teenager in high school, it’s a traumatic thing, regardless of whether you’re the most popular person in the class or the least popular, or somewhere on the spectrum in between because everybody at that age is terribly insecure. You’re not the coolest kid, you want to hang around with the cool because they’re clearly cliques and all that. In high school, this period from 14 to 18 is a difficult traumatic time or difficult time, not traumatic time, but difficult time for everybody in growing up. I think one of the reasons I ended up being a scientist was that I went from that typical middle school, high school malaise, and was taken out of that situation by chance and for summer moved out to Lawrence, Kansas, and lived in a dorm with all these other kids that were equally socially maladapt, probably.

Yet there we had this … It was like a great social environment and it was actually even interesting and I did all this science and I tend to care intensely about things that I do. I think internally I have a … There must be some competitive aspect to my character in terms of wanting to do, but I don’t automatically walking into a room or walking into a classroom where I didn’t think that I was the best student there. Yet I was very trended, I was very successful there because I go in and I do everything with this kind of emotional intensity that raises my performance and my ability to get things up to a high level. Then I was invited back to for another year and that was a reinforcement that yes, you can do things.

You can do things well, and this is a socially attractive circumstance to live your … You could do this for your life and people will pay you for this. It seemed I’ll do this. Yes, absolutely.

You found your clique.

Yes, of course. I can’t say that I necessarily planned to be a scientist, but I had the good fortune of having broad experiences and recognizing and being able to follow the things that I like. I was smart enough, I guess, to recognize this is something cool, this is something that matches me, this is something about who I am.

Illustrates how important it is to give opportunities to people at that stage in their development. A science camp type thing.

Eric F. Wieschaus: Absolutely. And it’s opportunities out of their normal life. You grow up with certain expectations and you grow up with an understanding of the world that is always limited in some sense. Being able to leave home, go someplace else, see other things, make other choices. I think it’s hard for me to say growing up in Alabama at that time, it’s probably special in itself but I think it would be true regardless of where you grew up that if you grew up in New York City, your experiences are still going to be limited regardless of where you are as a child. The opportunity to go away and do something kind of semi on your own, but in a somewhat protected environment is a great thing.

One sort of boundary you crossed was to move across to the East coast to do graduate work, and you chose Yale. Was that an easy choice?

Eric F. Wieschaus: This was 1969. I only applied to two places, to Yale and Harvard and this was because it was 1960, this was in the middle of Vietnam war and I was, I guess, politically active or semi politically active. This was in the anti-war movement. In Notre Dame, which is the university which I was at at the time, the movement had started pretty much on the two coasts. It was beginning to go in on my campus and the opportunities that I had as an undergraduate were to be politically active. I wasn’t really involved in the truly exciting things that were happening, and so when I went out to interview at the two places, Harvard and Yale, I got to Yale and met with many professors and talked with these people and it all seemed very exciting. It was like science and I could do this. It would be like graduate school and this would be exciting.

I took the bus from New Haven, which is where Yale is up to, to Boston. The day that I was in New Haven, the undergraduates at Harvard had taken over the university and the whole university had closed down. I arrived at Harvard for my interviews and they’d all been cancelled, and there was nobody in the biology department except for one young professor, so I actually spent that day with him. We walked around and saw the … and participated in some of the demonstrations, they were all very exciting. Then I laughed and I thought this Harvard must be an exciting place to be.

But then I have this side to my character where I … Harvard is exciting, but if I’m going to do science, I should probably go to Yale, and so I picked over Harvard. Next year of course the demonstrations were all at Yale, so it turned out to a great choice because I would’ve missed the demonstrations at Harvard anyways. Whereas the following year, 1970, was the big year for demonstrations in New Haven. I was there for that, but I didn’t miss anything. It was a good choice, many fortunate things throughout my life.

How about your choice of your research question? Because you found this area of embryogenesis, pathing of embryogenesis in flies, as a graduate student and have kept that question throughout your whole career. Which in a way is very fortunate, to have found a question that occupies you so well.

Eric F. Wieschaus: I suppose the really cool thing if you’d say what would you like to recommend. If you could recommend stuff to young students it’s really good if you find something that really fascinates you and it’s really hard. Because if it were really fascinating, and it was hard, you might solve it and then you’d have to find something else. Whereas for me, because the whole issue of embryonic development and pattern information and morphogenesis and form is so complex and operates at so many different levels, that the moment you decide for me, it was a decision looking at embryos that I knew that I wanted to understand. The process: how it is that a fertilized egg, single cell that looks simple can divide into many cells and then reshape itself into something as complex as our bodies is a process that … You can watch it, you can see it and if you watch it, you can’t help but be fascinated by it.

Can’t help to say, this is what I want to understand. What’s true is that you can understand it at a whole variety of different levels. In the famous experiments, the Nobel experiments, those are largely directed at trying to get entry points into the whole process of embryonic development by identifying genes that play specific roles at specific times at specific events, genes that are required for certain cells to do certain things at certain times. The idea of those experiments, if you knew all the genes, you could make a map or a logical scheme in a way for how the process occurs. But I think it’s still true that those genetic experiments that identify genes, they give you a map, but they don’t really explain things. They give you a strategy for understanding things and processes, but that’s all that it is. What you need, there’s still all these other levels where you use your previous experiments, you use those genes, you use your previous observations to build a better understanding of a biophysical understanding or a cell biological or biochemical understanding. But it all grows out from that map.

On this idea of being fortunate enough to choose a hard question that’s intriguing, there’s a talent involved in finding the entry point, in finding something. That allows you to access the question at all. The example that you raised with the Nobel Prize awarded work was a good one because there you undertook an experiment which was seemingly well, possibly impossible at the time, but certainly there was no guarantee that you were going to get the result you looked for, which was classes of genes that would control segmentation. So there’s a bravery and talent involved in choosing the right question.

Eric F. Wieschaus: Yes. I suppose it’s brave. Some people have called it brave and other people describe the experiment in ways that are different than the way that you see it yourself. I don’t waste time. It matters to me when I do things in the lab that they work and part of that is an ability to judge. Not only what’s interesting, but what’s interesting and what’s doable right now. What can I do right now? What’s the opportunity to maybe push forward a little bit on a problem to see this is something that is doable at this moment. I’ve come to realize that is something that drives me, the practical aspect of success, of doing successful experiments, more than the big question. This is a hard thing to parse out, but you could imagine, and I know there may be scientists who see and are driven by the big question and see things in terms of big questions. I’d like to believe that I have a little bit of that myself, but I don’t. I think probably I don’t, I probably don’t have it. That’s not my strongest suit. Maybe I bring some vague sense of big questions with me wherever I go. But my strongest suit, I think, as a scientist is being able to walk into a lab and see a novel or unexpected way of doing something or solving a problem, or being able to go in and say, this may seem hard to do, or this may seem convoluted, or this may seem chance, or this may seem brave, but I can do. And that’s a trivial I can. The questions here, and if I can measure this and get this thing done, I will learn something and something that’s really cool and interesting. My whole scientific career in part has always been driven by this sense of I can go into the lab and do something and produce something. I suppose, why I’ve never wanted to have a big lab. I never had a big enough vision to manage an army of postdocs and graduate students to solve something, to push forward, for the frontiers of knowledge, for that lack of vision, if you will.

Because what I like doing is going in and doing things myself, or working closely with people, a small number of students or postdocs in my lab to solve some problem, do something that no one’s ever done before. Bring level of understanding to a new level. I like the idea and this isn’t always true, but it’s substantially true that most of the papers, virtually all the papers that come from my lab, have parts in them that I’ve done. They can be small parts, they can be trivial parts. I’ll do anything to push an experiment for all amount, hand section 500 embryos. If I have to, for five afternoons in a row, the most boring part of an experiment, I won’t do the necessarily do the analysis myself, but if I can leap in and say, This is doable, we can push things forward, I’ll do this part right now. I feel comfortable with that way of being a scientist.

It’s a true collaboration between you and your students, then, you really working.

Eric F. Wieschaus: Yes. They never do what I want anyway. You might as well, kind of join, best to join forces. Sometimes when you ride these airplanes they have these little magazines and there’s little business management courses. I think, someone could explain to me how to run this operation in a more efficient way, that’d be cool.

On the top of collaboration, your work with Christiane Nüsslein-Volhard was obviously a wonderful sort of symbiotic relationship. What was it that the two of you brought to this? Are you just extremely similar or did you have differing skills?

Eric F. Wieschaus: I think we’re very in certain respects, we’re very similar. We’re both ambitious. We’re both somewhat self-contained in that we like and evaluate our success heavily by our own appraisal of what it is that we do. It matters to us. Each of us, it matters to us a lot. It matters to everybody what the world thinks and we’re social people in the world. Not totally, but we both have an internal standard for the quality of our work and a sense of gratification that the most important thing is to meet our own standards and to be happy when we’re happy with our experiments. Both intensely interested in science. She’s also visually oriented, so we both have certain common tools and strategies. For example, a lot of the immunogenetics experiments that we did in Heidelberg involve not only breeding thousands and hundreds, lots of fly stocks and collecting embryos, but a lot of it depended on our looking at them, and that we both took pleasure. We both take pleasure in beauty.

There’s this lovely picture of the two of you looking down the same microscope.

Eric F. Wieschaus: Exactly. I look at that picture and I see two things. One, that’s certainly true that we were both looking at embryos and enjoying the looking at the embryos. But the other thing, my memory of those times is we’re also competitive in the sense. The reality is that we had set up in any given time, thousands of inbred lines we were collecting embryos from, we work all through the morning trying to identify which stocks were appropriate to make microscopic slides up for examining the embryos. We prepared those and then in the evening, or the next morning, we would have a box or stacks of slides with embryos from each individual, fly embryos from individual mutant lines that we thought potentially would have a gene mutated or a gene would’ve been mutated that caused some interesting effect in development.

But most of it was just garbage or not interesting things, and so we would sit there at this dual microscope and you take a slide and we would both look, we put it on, and then our natural competitive sides, because if there was something there you wanted to be the first person to see it. I wanted to see it before she … She’s really good and she’s incredibly sharp eyes and intuitive. For me, it was like, you put the slide on and then you’re looking through stuff. A lot of it is on average, only one slide in 50 is going to be interesting. Yet you want to be the person who’s look. And it’s true that the way this’s competitive, we all have our favourite stocks in part and our favourite genes and our favourite phenomena.

I would love to tell you that this depended heavily on some inner insights, scientific evaluations for why runt is a particularly cool pair-rule gene or what /- – -/ is important for, but the reality is, always in the background for our scientific choices is this memory of the competition. If I happened to have identified runt before she did, embryos before recognizing them on the slide as something interesting and unique, then I, of course, I came to believe that that gene plays some truly central role in the process, because you’d like to imagine. We work very well in that way. I think we are also personally very close friends in that I think we understand each other very well, scientifically, but also personally in terms of … And value each other. Even though we see each other once or twice, I visit Tübingen once a year or so, we don’t see each other that much. We don’t collaborate anymore, we haven’t collaborated for 20 years. She’s still one of my closest friends in the world.

You were both in your first independent investigator roles when you did that work and I suppose one might have played it a bit safe at that point and just tried to get something under your belt to get the jobs. But obviously just that wasn’t …

Eric F. Wieschaus: I wasn’t smart enough to play things safe. No one advised us to play things safe. One thing that is probably true is that we didn’t talk to old scientists that much. That’s probably why the silly thing about me giving you this interview and God, if they’re any young scientists out there, they shouldn’t be watching this interview. This is pretty serious.

You feel like a young scientist to talk to.

Eric F. Wieschaus: I think basically it’s probably good to … We didn’t talk to many established scientists. We were aware that most of them thought that what we were doing was stupid or was not likely to work because it would evolve into lots of epiphenomena or things would be too complex or there’d be too many genes or not enough genes. Everybody that we knew, senior scientists that we knew in our field were … I can’t say they actually advised us not to do those experiments, but we knew that we were doing them and they weren’t there to be some obvious reason for that. It wasn’t that we were clever, they probably saw dangers or flaws that we probably didn’t see, which is I suppose a good thing about our age. The fact that we were also very self-sufficient and very interdependent, so talking to her was enough. I didn’t really have to take other people’s opinions very seriously.

There’s a parallel there with Brown and Goldstein, another great collaborative pair, who also say that each other’s approval was what they sought, in a way.

Eric F. Wieschaus: Yes, right, and that’s certainly true. Getting Janni’s approval is not easy and are not always easy. Particularly if things are … If you’re trying to do that with flawed experiments, that usually doesn’t work. It does set standards and you make choices because there’s enough people out there who are eager to impose or suggest standards to you that you as a scientist have the two choose who matters, whose opinions matter to you. I think we both benefited from making the right choice there. Her opinions matter to me and my opinion mattered to her.

Let’s turn to the choice of the flies and model organisms. You say you don’t like wasting time and I suppose the fly is the ideal model in that sense that the development lasts 10 days. You can ask a question, get an answer and move on.

Eric F. Wieschaus: Right. As an undergraduate, when I was learning science, I had my first exposure to flies. I needed money. I got a job in a fly lab making fly food and washing bottles, dirty fly bottles and maintaining fly stocks, stuff like that. I worked in a lab and eventually was able to begin doing genetics experiments. My professor Harvey Bender, who ran this lab, was interested in various aspects of fly genetics. To a certain extent they /- – -/ on adult characters, eye, colour, I think are eye morphology. I thought that was interesting. I like genetics. I learned genetics well, but I didn’t want to do that for the rest of my life. I, as an undergraduate, had taken courses in embryology and I’d seen frog embryos and fish embryos and chicken embryos, and that was the most beautiful thing that I’d seen.

I can remember sitting in the lab after everybody had got home and you do these fertilizations. You can do an in vitro fertilization with frog eggs, and you can see cells divide and you can see stuff happening, and I wanted to know that. I spent a summer, then at the end of my undergraduate period in the embryology course at Woods Hole I got to see many more embryos. That’s what I wanted to do. I wanted to look at embryos and I didn’t want to work on flies. When I went to graduate school. I would’ve been happy never to have seen another fly embryo in my life. The complication in my life, this was a chance thing, but in going to graduate school, my situation was somewhat chancy because this was in good 1969. I grew up in Alabama. Because of my opposition to the Vietnam war, I had applied for a conscientious objector status. This in my local draft board is a very conservative part, no one had ever done this before, and you had to apply for this status based on religious convictions, and at the time I was a Roman Catholic and I believed that my moral convictions were grounded in my … I had tried to apply for this thing, and I failed. I was in the middle of all these legal procedures and I was into reading prison literature because I was convinced that I was going off to prison, but I’d also applied to graduate school and was admitted to graduate school. All this was going on.

Harvey Bender, who was my boss in this fly lab liked me and cared about my future and was concerned about me going to graduate school with this whole huge burden of the Vietnam war and the conscientious rejection and all this stuff, my legal debacle in Alabama. He wrote to the only person whom he knew at Yale, which was Don Poulson, and told him there was this young person coming as graduate student and would he take him under his wing? When I arrived at Yale, Don Poulson, who was about 60 at the time, came and up to me and took me under his wing and took me into his laboratory and was very kind, so kind that I didn’t have the heart to tell him that I never wanted to see another fly lab. I never wanted to see another fly lab or flies in my life. It was good that that happened. I didn’t know who Don Poulson was, Don Poulson was 60 or something at the time. In the 1930s, as a graduate student at Cal Tech, he’d gone to Cal Tech to biochemistry, but got sucked into a fly lab at Cal Tech, and in the 1930s did all of the embryology of Drosophila, all the basic descriptive work, and also all the original work showing that genes controlled the way embryos developed.

He was the only person … This was an important set of experiments, but this was not where science was in 1960. I ended up in his lab, at that point. I didn’t know that flies had embryos. I said this often, I don’t know where I thought flies came from, maybe from rotten flesh and spoiled lasagne or something. Some people thought so. I didn’t realize that flies had embryos or that if you looked at a fly embryo, it would be every bit as beautiful as a frog embryo or a chick embryo, and I learned that from Don Poulson.

You inherited this sort of semi-secret stock of knowledge?

Eric F. Wieschaus: Yes. Then Poulson didn’t want a graduate student. He was being kind to me, but he didn’t want a graduate student. My memory of Paulson mostly is him reading his papers. Then I would see him, this old man, backing into his office when I was coming with all of “This”, and “You said this”. Poulson, after about a year and a half, arranged for me to switch labs and move into the laboratory of a young assistant professor who’d just been hired at Yale, Walter Gehring from Switzerland. Poulson, I think with a lot of relief arranged for me to go over to Walter Gehring’s lab. Walter’s lab at the time was a great, lucky thing, he’d just been hired. His lab was empty and I was his first graduate student.

He just found a technician himself. There were just three people in the lab, and I worked with Walter for the first year side by side, we would transplant cells and do things. His lab gradually grew, and then after about a year and a half, he decided that he was going to leave New Haven in Yale and go back to Switzerland and asked me if I wanted to finish my graduate work in Switzerland with him in his lab. I said, Yes. I’d never been out of the United States before, New Haven was the most exciting place that I’d ever been in up to that point that I got on an airplane and flew over to Switzerland, stayed in Europe then for 10 years. But the whole fly connection, why I ended up working on flies was just extraordinary good luck, because the ability to do genetics on an embryo was the crucial thing that was needed at the time. Many people did genetics and many people did embryology, but by chance, there I was, one of the few people in the world, a small, small little set of people in the world who knew that flies had embryos that were beautiful. Who knew enough fly genetics to think about how one could approach the problem from the standpoint using the past 60, 70 years of Drosophila genetics to solve something that interested me more deeply, which was not genes and was not genetics, but how embryos developed.

Again, it’s the peculiar interplay of chance and talent in having the right tools at the right time the right question is.

Eric F. Wieschaus: And saying, I want to do this thing. This thing is doable. Go for it.

We’re sitting just up the corridor from your small lab. I wanted to finish by asking you about the students you choose to work with you. What do you look for when you’re picking people?

Eric F. Wieschaus: I think it helps if they’re smart, at some level you’ve got to bring that to the table. I tend to abandon students fairly quickly in the lab, I would rather that they do experiments that they care about. On the other hand, this is odd. I don’t run a lab so that other people can do experiments that they care about, I’m not that generous. I want to care about their experiments and participate in them at some level. The best thing in my best students always started out with a certain level of independence, but also working with me and then ended up someplace totally different than I would’ve predicted with a set of results or a set of experiments that I didn’t really anticipated, made me rethink what it was that I thought we were doing.

That’s really what you want from students or postdocs in your lab, that they do something that I can take part in because I, like I said, I don’t run my lab so that other people get the opportunity of doing science. I run my lab because I want to do science, but I want to work, so they have to be able to convince me that it’s something worth doing and that I’d be happy to sort flies for them or collect embryos or do some part of this thing. But I’m happiest if they assume responsibility for it. I think that’s the critical thing. I suppose what it means is that I don’t want to assume responsibility. I suppose that really means is I don’t want to assume responsibility for their failure. If they fail, I don’t want it. I don’t want the responsibility of making somebody else’s career. I don’t want to provide a vehicle and a responsibility for doing this and this and then the thing will work if you do what I say. I would rather work with people who, even though they’re at a different stage in their career, are essentially independent scientists with whom I can collaborate.

It’s the ability to spot those people because you don’t have a high three-foot screening where you’ve got lots of students and you can just pick the ones you like.

Eric F. Wieschaus: Yes, I think one of the things it’s probably also true that it’s not even a screen, it’s also a matter of adaptability because everybody you work with is different. It’s not like I would look for a certain set of qualities and then only choose people who have those qualities. It’s more that I have to choose some among the large range of qualities that are out there that I could see there’s a potential for me to interact with or to shape myself in response to them. I probably don’t really shape myself that much.

Sounds good.

Eric F. Wieschaus: In a certain sense, I do, I shape myself with a response to them. I am a reactive person, meaning I talk with people and I respond and I’m empathetic. I’m not internally driven enough to expect the world to go through all on my own little tracks. I do adjust my behaviour all the time when I am talking to people. I’m a social human being. In lab it is not so much that it has a certain format of person who will interact well with me, because I kind of change how I talk with or work with people depending on, because science is so peculiar that it is so unpredictable what are the qualities that are required at any moment for any particular problem? I know scientists and this extraordinary heterogeneity of scientists who are successful and some of them are shy and some of them are loud and some of them are showy and some of them are risk takers and some of them are all of these qualities among the really successful scientists that I know.

Some of them seem really, really smart, and some of them don’t necessarily seem so smart, but they really are. This whole heterogeneity of scientists out there. In part what we do as scientists, and this is the thing that I think most people don’t understand about science is how much of a social activity it is.

That’s true. The image is of the lonely person.

Eric F. Wieschaus: The lonely person in the lab and that’s not … The way science works is heavily through a whole variety of different kind of social interaction, some of which are competitive. Either you have your competitors, you have your semi competitors, you have your friends, you have your supporters. All of this kind of a social network in science that reinforces and forces all of us to maintain high standards for our productivity, for experiments, subjects us to criticism at a whole variety of levels. In part, in running a lab, what you want to have is a social structure that mimics that flexibility. You’d like to have people in most successful labs run that way and that they have different kinds of personalities in them. They are extraordinarily supportive places where scientists interact with each other and support each other and criticize each other’s experiments, like a little mom and pop store atmosphere. Small business, a lot of interaction, criticism, sometimes bad emotional blood, more likely like a family where you get a bunch of personalities in a room and they have to keep this boat afloat.

People are always talking about the role of science in society, but this is the society of science.

Eric F. Wieschaus: It is something that when I was a child in Alabama, I didn’t know existed. I didn’t know what to be a scientist was. I think that one of the things that I learned at Kansas or going off and being able to work in a laboratory is, at Kansas or being able to work in laboratories at Notre Dame, is how extraordinary gratifying it is for the social aspect that we’re probably all stuck back in our human evolution back. We don’t evolve rapidly if we’re all still biologically stuck back in this hunter gatherer, small tribe stage in terms of our personal interactions. We gravitate towards that social structure and the science, the laboratory academic science, the way we do it now is probably a pretty close approximation for little tribes and little groups of people out there trying to find nuts and edible fruit out in a jungle at that same level. It’s what we’re evolved for.

It’s a lovely idea. There’s a lovely guy called James Curnow who makes furniture. He wrote a book about a challenging time in his life when he decided that he wasn’t going to make any money doing this. He came back to the idea eventually that all he could do was make the furniture he believed in, and somehow things would be right. It sounds like the approach to start, isn’t that different for that? You do the experiments you think are right.

Eric F. Wieschaus: It’s hard nowadays. Maybe I was more naive and I didn’t know as much as young people know now, because of the web, because everybody knows the job market, everybody can follow my postdocs. My graduate students are probably wiser and probably base their decisions on more information and more calculation than I do or ever did. In a way that’s good, but in a way it’s bad because you can’t know everything. The one thing that it’s very hard to know is your own personal quality. What’s hard is you can make the calculation on the average job prospect, and you can make your calculations by what people tell you you should do on average, but that’s not going to get you anywhere. The strength that you bring to science is your own personality, your own weird combination of abilities, my visual orientation or my curiosity or some intuitive ability with math at some level, those weird things that you piece together that makes you dR and different from anybody else. That weird combination, that unusual combination that’s distinct for each individual scientist makes it very hard to calculate career choices based on averages.

All this extra information that’s out there that is in theory helpful, I think might interfere with what’s the strongest thing, strongest determinant, which is this internal personal drive and internal personal necessity of matching who you are in terms of gifts and abilities and desires with a particular scientific problem, with a particular career choice. I think I had the benefit of being internally driven and making almost all of my choices based on that.

And not having the impediment of too much information.

Eric F. Wieschaus: And not having the impediment of too much information. Absolutely. I look at some of the things that I did and I would be very shy to recommend those to anybody, but they were the right things for me. I think that internal sense is something that you have to rely on, when you’re young, as well as when you’re old. You have to rely on it throughout life, I think. If you’re going to make choices that are going to contribute to your happiness or your success, you have to rely on that internal sense of who you are and what matters to you.

That’s a good piece of advice.

Eric F. Wieschaus: Yes.

I couldn’t have been happier with that. It was marvellous stuff. Thank you very much.

Eric F. Wieschaus: Yeah, absolutely. So what do we do now?

We stop. Okay.

Did you find any typos in this text? We would appreciate your assistance in identifying any errors and to let us know. Thank you for taking the time to report the errors by sending us an e-mail.

To cite this section
MLA style: Eric F. Wieschaus – Interview. NobelPrize.org. Nobel Prize Outreach AB 2024. Fri. 19 Jul 2024. <https://www.nobelprize.org/prizes/medicine/1995/wieschaus/interview/>

Back to top Back To Top Takes users back to the top of the page

Nobel Prizes and laureates

Eleven laureates were awarded a Nobel Prize in 2023, for achievements that have conferred the greatest benefit to humankind. Their work and discoveries range from effective mRNA vaccines and attosecond physics to fighting against the oppression of women.

See them all presented here.
Illustration

Explore prizes and laureates

Look for popular awards and laureates in different fields, and discover the history of the Nobel Prize.