Albert Lasker
Basic Medical Research Award

An Interview with Lee Hartwell
Interview by Dr. Rochelle (Shelly) Esposito

In an October 1998 interview with Dr. Rochelle (Shelly) Esposito, a professor of molecular genetics and cell biology and chair of the Committee on Genetics at the University of Chicago, Dr. Leland (Lee) Hartwell discusses how he developed a fascination with science and cellular research. He talks about his work and its value to medicine, his teaching philosophy, and what genetic developments he believes will occur in the not-so-distant future.

Part 1: From a Non-academic Beginning to the Halls of Cal Tech
After early work studying mammalian cell biology, Dr. Hartwell sought a new focus. Frustrated with the prevailing models framing mammalian cell research, he realized yeast cells presented the ideal environment for investigating mutant cells and DNA replication.

Esposito: On behalf of all of us who have been impacted by your work, I want to convey our warmest congratulations on this wonderful honor and award. We're really pleased and delighted, and it's very richly deserved. I'd like to ask you, can tell us what this award means to you and what you feel it's recognizing?

Hartwell: Yes. It's, of course, very exciting and rewarding to me. It's always terrific in your career to feel like you've made a contribution, and that's the gift the Lasker committee is giving me. I think they're recognizing the whole field of cell cycle research and yeast genetics. I feel fortunate to have been in on some of the very early phases of that work, but it's really the work from hundreds of labs and thousands of students that have brought it to the stage where it's deserves this kind of recognition.

Esposito: Can you tell me what, from your perspective, are the most significant contributions that you think your lab has made to this field?

Hartwell: I think it was perhaps in seeing that a study of cell division, even though it was motivated by an interest in human cells and medical problems like cancer, needed to be explored in a much simpler system using genetics as a powerful tool. It was in attempting to place the groundwork there, that's probably one of the major things we contributed at the beginning.

Esposito: What I'd like to do in the next series of questions is address how this all came about. Maybe on a personal note you could begin by telling us a little bit about your family background and how you first got interested in science? I know this is going back a bit, but it's always interesting, I think, to others, to know what the motivating forces are that drive us to the discoveries that we make.

Hartwell: I came from a family that was very nonacademic, so I didn't recognize at an early stage the clear interest that I had in science as a child. Looking back, it's easy to see now. I always collected bugs and took things apart and spent time at the library trying to learn things about radios and astronomy and various stuff like that without noticing that my peers weren't spending their time the same way.

I don't think I would have ever gotten the opportunity to spend my career in science if it hadn't been for a few key teachers along the way. [There were] a couple in high school that recognized my interest and ability in math and physics, and gave me extra work and encouragement, and a counselor I had in junior college—I went to Glendale Junior College for a year—who also took an interest in me and got me to interview with a professor from Cal Tech who was visiting. It was through that interview that I eventually ended up at Cal Tech and discovered a whole fabulous world of science that I really didn't even know existed.

Esposito: I know that your undergraduate career at Cal Tech was a transforming experience for you. Can you tell us what the atmosphere there was like and how it really set the stage for the future directions that you wound up taking?

Hartwell: Cal Tech was just an unbelievable sort of fairy tale place for me. You were spending your time thinking about really interesting scientific issues, and the faculty there treated the undergraduates like they were colleagues rather than students. It just gave me a sense of involvement and the possibility of participating in science, sort of an invitation, I guess I would say, that I look back on and just cherish those years. A particularly influential individual to me was Bob Edgar, who worked in Max Delbruck's group and, of course, did all the work with Bill Wood on phage morphogenesis. But I can still remember the afternoon when I was walking by Bob's office, and he stepped out and pulled me in and explained to me a neat idea he had for determining how all the genes and phage function. To think that an undergraduate would warrant that kind of collegiality just made it a very, very special place.

Esposito: It sounds like a wonderful environment. You were an undergraduate working in his lab. How does that come about?

Hartwell: The neat thing about Cal Tech was that they really encouraged people to do research, and so as an undergraduate I did research the whole time I was there—I mean both during school and in summers. There were so few undergraduates compared to faculty that you could essentially work for anybody there you wanted. They were always happy to have a student come in and work. I felt pretty much like it was a graduate level experience because I did so much research as an undergraduate.

Esposito: Did you work in several different labs, or did you find your way to Edgar's group early on?

Hartwell: I worked in several different labs. I worked for Hildegard Lamfrom for a while, who was trying to figure out what messenger RNA was. I worked in Renato Dulbecco's group with Howard Temin for a while and then in Delbruck's group.

Esposito: Did your interest in the cell cycle originate at Cal Tech or later when you went to do post-doctoral work?

Hartwell: It didn't really come until I was doing post-doctoral work. As an undergraduate I guess I was interested in phage and then as a graduate student I was interested in gene regulation. Then when I was thinking about becoming a post-doc, it seemed like the appropriate thing to do was to pick a problem that you were going to spend your career working on, something that wasn't understood yet. I decided to work on cancer and cell division, growth control sorts of things. I went to work with Renato Dulbecco and came to a tremendous interest in the problems there. I had another wonderful experience with a colleague, Marguerite Vogt, who is just a delightful scientist who is always interested in each new theory about cancer. She is a person who has developed a sort of artistic love for cell culture and what cells are. That was a big experience for me, too.

Esposito: I guess when you went to do your post-doctoral work you really had in mind by your choice that you wanted to work in cancer and maybe cell cycle and cell division. Did this stem from your studies on gene regulation when you were at MIT? Also, I kind of transited through your graduate work without asking how you wound up at MIT, and what were the problems that were being addressed when you were there? What were your thoughts and the influences on you at the time you were there?

Hartwell: At MIT, that was a pretty neat experience, too. The reason that I ended up there was because I went to Bob Edgar and said, where should I go to graduate school? He said MIT, and so I did. One of the things they encouraged undergraduates to do at Cal Tech was to read in areas that you wanted to study in. And so every quarter I took a reading course under a faculty member's direction. I read a lot about gene regulation, so I knew when I went to graduate school I wanted to study gene regulation. And so when I went to MIT I knew I wanted to work with Boris Magasanik and was fortunate enough to be able to do so. I think the main thing I took away from that experience was how Boris just let you find your own way.

He would come by every afternoon and ask you how your experiments were going, so it sort of kept you at this feverish pace for having results every day. But he never told you what to do. He'd always just asked you how things were going, and he would make suggestions, but he made it clear that you were plotting your own course. That was very comfortable for me having already had so much research experience. But I think it also really helped me develop that sense of: I was the master of my research, and I had to find my own way.

Esposito: I had a similar experience. I wonder if when you look back and compare the way you were trained and the climate in which science was done to the way it is now, whether there was, in reality, more freedom to explore and follow your own instincts. What's your thought on that?

Hartwell: My experience and my colleagues' is that there is tremendous anxiety about getting grants and keeping your career going, so that there is much greater, often, direction of students to fill necessary goals, to get the right experiments done for the next grant and the paper out and that sort of thing. I never experienced that kind of pressure myself, and I must say I never put my students under it. I think I work with my students the same way I experienced science, where they're in charge of what they do, and we hope for the best. Fortunately we have been lucky enough that that has worked. I do think the climate is very, very different now and not one that I would thrive in if I was a student and feeling like I was "doing project 17 on somebody's RO1 grant."

Part 2: A "turning point" Conversation Leads to a Shift in Research Focus
After early work studying mammalian cell biology, Dr. Hartwell sought a new focus. Frustrated with the prevailing models framing mammalian cell research, he realized yeast cells presented the ideal environment for investigating mutant cells and DNA replication.

Esposito: Tell me about when you first decided to make the switch into working with yeast. When did that happen? Why did it happen? What was your goal in switching from mammalian cells to yeast when you left Dulbecco's lab?

Hartwell: It's one of those things where I have learned over the years that often the most important generalization we can draw is what not to work on, what not to be interested in, and, thereby, what to focus on. Also, to have times when you know that you're puzzled and frustrated and take time to let that be until some idea matures. I left Dulbecco's lab actually quite frustrated with the whole problem I was supposed to work on. I had actually gotten a grant to work on growth control and mammalian cells, but I was frustrated with the techniques and experimental paradigms that were available at that time to approach the problem.

I had moved to the University of California, Irvine, and had several months while I had ordered equipment and was waiting for a few things to come in before I could get a lab up and running. I had some time to think and spend some time in the library and talk to some of my colleagues. It was a really turning point sort of conversation, I remember, with Dan Wolf, who was also a young assistant professor there, where I expressed this frustration. He said, "Why don't you work on a eukaryotic cell where you can do genetics?"

I thought, "Great idea, why didn't I think of that?" I went back to the library and just looked for something like that, and came across a lot papers on yeast, and it seemed like an organism that fulfilled all of those needs. I hadn't had any experience with that organism, but I called up some of the people in the field, Herschel Roman being a prominent name (you were in Herschel's lab then), and I just started asking about the organism and how do you work with it? And Herschel in his very generous way invited me up to talk and see how things were done. So, that's really how I got started.

Esposito: At that time yeast was really in its infancy. Did you find the transition easy to make?

Hartwell: It was very sophisticated as a genetics organism. But most of the people working on it were asking questions about recombination and mutation and things like that. It wasn't being used very much for cell biology. An exception was Don Williamson, who had done some work on cell division in yeast, and that was a stimulus to me. As far as working with the organism and trying to do what I wanted to do, I was actually rather fortunate in that I treated it like it was bacteria, and for the most part, that got me through. It was only...it took a few years before we really began to appreciate the differences that made it more relevant from a sort of cell cycle point of view.

Esposito: When you first started, what was your goal in isolating temperature-sensitive mutants?

Hartwell: It was modeled exactly after what Bob Edgar had done with T4. He said, "Let's find out what all the genes do. We'll do that by isolating mutations in all the genes and then seeing what goes wrong." In order to do that, he used temperature sensitive and amber mutants. So, temperature sensitive was really the only way to approach essential genes in a cell. It was natural from that paradigm to just isolate a lot of temperature sensitives and then use a different variety of techniques to figure out what might be the primary defect in different mutants.

Esposito: As I recall, your original goal was to study DNA replication and what was involved in triggering the S phase itself. Is that correct?

Hartwell: That's right. That's what I was focused on coming out of Dulbecco's lab. First initial experiments were to isolate a bunch of temperature-sensitive mutants, shift them to the restrictive temperature, and look at the RNA/DNA synthesis, and look for mutants where DNA synthesis shut off before RNA or protein. We found a few mutants like that. Along the way we found a lot of interesting phenotypes having to do with protein and RNA synthesis, so we spent a few years chasing those down also, because I had colleagues—Calvin McLaughlin, who was interested in protein synthesis, and John Warner, who was interested in ribosomes—that we were able to collaborate with.

But you're right. The real passion for me was DNA replication, and we didn't find very many mutants that looked like they were DNA replication mutants. It was only later when we began to look at cells by photo microscopy that we really were able to get into the cell cycle as a global problem in a productive way.

Esposito: I wanted to ask you two questions related to that. The first is that, at the time at which the temperature-sensitive mutants were being isolated, going from isolating the mutant to actually finding the function that was defective was a daunting task. How did you feel about that? Did you feel that you would be able to do this? Did you have ideas about how to do this? What was your approach there?

Hartwell: The only real paradigm was to have a mutant and be able to make extracts where the process of interest occurred in vitro and then show that the mutant was defective in that, and then use the mutant extract to purify the wild type function. That was the paradigm. That sort of thing had been done in DNA replication and bacterial systems, so I guess that was our thinking. But once we got into the cell cycle and beyond DNA replication to a lot of other processes, it seemed pretty hopeless to actually ever be able to get mitosis to go in vitro, and spindle pole duplication, and things like that. I think we were...it wasn't at all clear that there was a path to really get the kind of answers that you wanted.

Esposito: Let's go back to the original idea of obtaining cell cycle mutants and ask how that idea originated. Who was involved? How did the idea of using the bud as a time marker for the stage of division come about?

Hartwell: That's one of these wonderful stories of serendipity, where I had an undergraduate working in the laboratory, Brian Reid. My experience of working as an undergraduate in laboratories was they always gave you some real wild project that you could just pursue on your own and have fun with. The problem that I had suggested Brian work on was looking to see if he could find in yeast the phenomenon of cortical inheritance that had been described in paramecium by Tracy Sonneborn, a phenomenon where surgically he took a piece of the cell wall and turned it around, and that pattern was inherited. We had yeast mutants that formed odd shapes at the high temperature. Brian was to take these mutants and see if, once the shape of the cell changed, that odd shape would be inherited when the cells were shifted down to the permissive temperature.

It didn't take him very long to discover it wasn't inherited, and we said, "Let's look at how the cell shifts from an odd shape to a normal shape. Let's look at the intervening divisions." So, to do that, he needed to look through the microscope, and he actually started taking photographs of the cells. I think it was one of these "the lights going on" experiences, when we sat around looking at these photographs, and you could see the bud and the small buds and the big buds and realized there was a tremendous amount of cell cycle information staring us in the face.

Esposito: Then you just started collecting mutants that were defective?

Hartwell: Yes, so then he started looking through just mutants at random. And about 10% of the mutants made sense from the point of view that the cells were originally asynchronous in the cycle, but had a certain stage of the cycle where they became defective and then became morphologically synchronous at the high temperature. That was the foot in the door. We just had a wonderful four or five years when Joe Culotti and Lynna Hereford and Brian Reid and John Pringle and I just studied cell cycle mutants.

Esposito: So within that first group the major conceptual advances of termination points, execution points and start pathways all emerged and seemed to follow each other very quickly.

Hartwell: Yes, it was in the first five years that much of the future questions that my lab followed for many decades were formulated--as a result of just looking at these mutants.

Esposito: How did the work on mating in yeast, which you spent quite a bit of time also studying in parallel to the cell cycle, how did that fit into your interest in cell division controls?

Hartwell: That came about very early as well because Wolfgang Duntze in Germany had reported that mating pheromone stopped cell growth. We were interested in whether it affected the cells at a particular stage in the cycle, and actually he came out and visited and brought some of his mating factor with him, and we did experiments just like we did on TS mutants. Sure enough, the mating factor arrested the cells in G1, and, that then led to looking at, in normal mating mixtures, did cells mate in G1? And yes, they did, and that led to looking for the other mating factor that must be complementary in inhibiting the other cell type in G1. Then we got interested in exactly where in G1 this mating factor was acting. The mating factor work really grew all out of the cell cycle and its role in controlling cell division.

Esposito: In it's own way it also was quite significant, because it really laid the groundwork for understanding signal transaction pathways.

Hartwell: Yes, we isolated a lot of temperature-sensitive sterile mutants, mutants that couldn't mate, many of whom turned out to be components in the signal transduction pathway. Vivian McKay had isolated some of the mutants prior to that. Ours were a little more useful in some sense because they were conditional so you could do genetics on them at one temperature and then study their defects in mating at a different temperature. We got interested in the receptor, but again, that's an example of many, many labs contributing to something that eventually turned out to be a major story. I just want to acknowledge Bob Edgar again.

It's funny, when I was an assistant professor at UC, Irvine, after about a year, and I had all these TS mutants. He [Edgar] came through and visited, and one of the things he said to me was very memorable. He said, "Well, these are really interesting mutants. You're not going to be able to work on all of them. You'll learn a lot more about them if you share them with other people. "That was just so prophetic, because we did and indeed, we learned about them from other people's work.

Part 3: Methodical Research Opens an Important Door; What's next in Genetic Research
From investigating termination and execution points in yeast, Dr. Hartwell's work shifted to the dynamics of signal transaction pathways and dysfunctions in cellular mating cycles. Here, Dr. Hartwell explains why yeast systems will help in deciphering the human genome and previews his next avenues of research as well as what he views as the next major issues in genetics.

Esposito: Let me jump forward a number of years. After the original very important period in the early 70s, when the whole cell cycle paradigm started to emerge, most of the activity that followed involved studying the mating process. Then, only later, did the checkpoint idea start to emerge. Could you give us some insight into how that idea developed which ultimately provided a critical key to understanding how the cell cycle proceeded?

Hartwell: That was just another good example of turning a student loose on whatever they were interested in. Ted Weinert, who had joined the laboratory as a post-doctoral fellow, said, "You know, I'm interested in regulation. I want to study regulation in the cell cycle." The more we talked, I recalled what seemed like an obvious case of regulation where when you irradiate cells, they arrest in the cell cycle, so as a result of DNA damage, cells arrest. He started looking at that phenomenon, and it was out of that the checkpoint idea came, because he discovered there were mutants that didn't arrest the cell cycle in response to DNA damage. So they identified the components responsible for that checkpoint.

That initial work on radiation response solved a major paradox for us in the cell cycle because we had found that almost any mutation that affected some component of the cell cycle even the polymerase or the spindle or anything arrested the cells. And as the paradigm was developing, at that same period of the cyclin-dependent kinases, it was becoming clear that there was no need for that. That if the cyclin-dependent kinase were triggering the events in the cell cycle, with a defect in the event itself, like the spindle or DNA replication, there was no reason to expect it to stop the progression of the CDK cycle. In fact, in embryonic cells, it didn't. So, there was a real paradox there of why all the cells stopped. And it was this discovery of checkpoints that eventually explained that.

Esposito: Using a simple model system to get at the cell cycle proved to be a really important insight in your work. Do you think that yeast as a model system is going to continue to play a central role in understanding pathways of gene function in higher systems as we move to an era where the human genome itself will be sequenced very shortly? Do you think there will be a shift to working with higher systems themselves?

Hartwell: I think the model systems like yeast are going to continue to lead the way for a very long time. I found myself over and over again when I start thinking about a problem, a problem that may exist in higher systems, like cancer or something, that eventually, as I begin to think about what the fundamental issues are, I can always approach the fundamental issues in a system like yeast, and I always go back there. We're beginning to see now, as the genome of yeast is complete, and people are beginning to use whole genome approaches to problems, that there is just a renaissance. That even though we may know a lot about what individual genes do, we know almost nothing about the complexity of how these pathways interact. And issues of evolution, and issues of robustness, and all kinds of things that characterize living cells. My feeling is there is so much left yet to learn about something as complex as a yeast cell with 6,000 different proteins in it, that fundamental issues of biology will continue to be fruitfully explored in those systems where there's so much power.

Esposito: What excites you most now? What research directions are you planning to pursue?

Hartwell: I've gotten very interested in issues of the system, the complexity of the cell. The point at which I decided to try to think about that again comes from looking at humans. As I look at human biology and compare model systems, the thing that strikes me that is so different about human systems is the fact that they're outbred, and you have all this genetic variability. No two organisms are the same. Yet, everything we deal with in the model systems is isogeneic, genetically inbred. That seems to me like a really fundamental issue. We're just starting to think about what does genetic diversity, natural variation, mean to biology? How can we explore some of those fundamental questions in yeast?

Esposito: Why did you take on the directorship of the Fred Hutchinsen Cancer Research Center? What are you trying to accomplish, and how does that interface with your own research interests now?

Hartwell: There are two answers to that question. And I'm not sure which is really the strongest motivating one. The simple scientific answer is the yeast cell cycle work and our interest in the instability of the genome in cancer cells, and what controls the stability of the genome? The fundamental issue in cancer, many of the fundamental issues, can be studied in yeast, and I think that new technologies of genomics that are really ready to make an impact can allow us to have a real impact on human cancer. That's the scientific answer, that we're "ready," to learn things from the models in a real human venue.

But I suspect an emotional answer is more correct. That is, I'm at a time in my life when I'm beginning to realize that people, and them trying to accomplish things and working together is more interesting than science. I like the aspect of being more involved with dealing with people in an institution and peoples' careers and things, people that are trying to accomplish something with their lives and interact. I just find the human element, I think, of playing the game of science more fun than the science.

Esposito: In some ways it's also dealing with complex interactions but at a different level!

Hartwell: Yes, we are, after all, biological systems!

Esposito: I want to bring the interview to a close by asking you what you think the key problems are going to be in genetics over the next decade or so.

Hartwell: I think it's the incredible complexity of living systems. Most of our thinking is in terms of a gene or a couple of proteins interacting, or a simple pathway. Cells are just so incredibly complex and our methods for looking at them are so removed from what's really going on. The way that we decipher a pathway, which is most of what's going on in genetics now is to look at terminal states of a cell where something has been altered. We're going to be developing methods for looking in real time, at space and time, at things that are going on in a cell at a molecular level, and just the complexity of everything that's interacting with one another. It's exciting that now there are an increasing number of technologies being developed that are beginning to allow us to approach things at the level of complexity of thousands of elements rather than just a single one.

Esposito: Congratulations again. I wish lots of luck in your future work. You've really been an inspiration to all of us.

Hartwell: Thank you. By the way, I want to mention that I got my original yeast strain from you. You played a big role in this whole thing.

Esposito: It was an honor to give it to you!