Interview with the 2001 Nobel Laureate in Physiology or Medicine Leland H. Hartwell, at the 57th Meeting of Nobel Laureates in Lindau, Germany, July 2007. 

Lee Hartwell, co-recipient of the 2001 Nobel Prize in Physiology or Medicine together with Tim Hunt and Paul Nurse, welcome to this interview. If I mention the word mentorship, what comes to mind?

Leland Hartwell: I think, as laboratory scientists, maybe most scientists, we work very closely with students, often in small groups, I never had more than about eight people in the laboratory. That’s a very intense relationship that’s where a person is learning to do science over many years, for a graduate student it can be as many as six years, for a post doc it can be many as four or five years. Those people come into that situation without knowing anything about how you do science. The way you learn how to do science is through that relationship and what the ethics and principles and judgements are, so it’s an extremely close mentoring relationship. I know everything I use and apply in science I learn from the people I work closely with.

When you bring students into the lab what do you look for in them?

Leland Hartwell: With graduate students I would take anyone into the laboratory that was accepted by the department, because it’s a pretty good department and the quality standards were pretty high. I don’t think that the criteria we have for judging students prior to them getting into the laboratory and doing science are very good so it’s a matter of giving people a chance to see what they can do and in my experience about half of them are cut out to be scientists and about half of them aren’t.

Is there anything in particular that distinguishes early on those that are cut out for it?

Leland Hartwell: I think it’s a couple of things, it’s a strong sense of determination and commitment and it’s also an ability to think for themselves. Then there’s for laboratory science a factor of what people call good hands where you can make things work or you can’t, and nobody really quite knows what that is but those three things are pretty critical. The sense of self confidence that’s needed to make your own judgements and even to argue with your mentor about whether some thing’s important or meaningful, an experiment worth doing, those are very good signs when a student’s willing to argue with you. Whereas primarily in undergraduates we just judge intellectual abilities by whether they pass tests or not and I didn’t even mention that I’m sure that’s an element as well, but these other things are really important in laboratory science.

Maybe the last point is a given.

Leland Hartwell: That’s right anybody who’s there probably has that quality yeah.

When you organise your lab, what do you keep in mind about the environment?

Leland Hartwell: For me it’s primarily intense interaction about ideas and results and in a sense I don’t organise the laboratory. People don’t work in teams in my laboratory, everybody has their own project and they don’t take up where somebody else left off. They come in, they talk to people about what’s going on, they think about, read about things that we’re interested in and come up with some idea, try it out. It usually takes three or four ideas before a student can find something that really opens a door.

But they have to find their own idea?

Leland Hartwell: They have to find their own. We’ll talk about ideas, there’s ideas floating around but I think the critical thing is being able to experimentally open a new door. That’s a huge challenge for new graduate students and I think that’s where some make it and some don’t. Frequently when you try something doesn’t work, so it often takes three or four or five projects before you find something that works and you can’t spend a year or two on each one, so you’ve got to be able to get an idea, think of a critical experiment, do work within a few months, find it doesn’t work, move onto the next thing. I think that’s really critical for students who are going to do science on their own because they’re going to have to open new doors several times in their career. Once you open a door you may have several years of productive research but eventually you’re going to have to open another door.

You have to establish that confidence that you can do it I imagine.

Leland Hartwell: Right, exactly and so you have to do it for yourself.

You’ve said already that people don’t work in teams but is there any physical principle by which you organise the people in the lab, do they all work closely together?

Leland Hartwell: No.

No? It just happens?

Leland Hartwell: It just happens.

I wanted to start by exploring your own scientific beginnings. From your autobiography that you submitted to the Nobel Foundation you describe a childhood with some interest in science but that didn’t really kick off until you got to the end of high school when you became a physicist really?

Leland Hartwell: Right, I never knew I was interested in science, I grew up in a family where no-one had gone to college so I didn’t know anything about academics. Through the first junior high school and half of high school I was pretty rowdy – a lot of sports, lot of hanging out with guys and cars and girls and that kind of stuff. I got tired of it, mid-way through high school and I guess I felt like it wasn’t very satisfying and switched schools to change the environment but not knowing that I really wanted to do anything intellectual. I was just very fortunate and I find over and over again when I talk to people who are successful they often point back to a teacher that was the critical influence. Certainly was for me, it was a physics teacher who recognised I had some ability and would stimulate me with extra problems and give me hard problems to solve and I really got hooked. It was a lot of fun and then I got really interested in school and academics and math and physics and things and then I found I could do very well in those things, but because I had only had a year and a half of decent grades, I went to a junior college for a year.

A junior college is a stepping stone between school and university?

Leland Hartwell: Yes, junior college in the US is usually a two-year college and people then will go from there to a four year college. Again I got lucky because I was thinking I’d probably go into engineering but I had a counsellor who grabbed me by the scuff of the collar one day and said Listen you’ve got a recruiter here from Caltech and you’ve got to talk to this person. I said No no, I don’t want to talk to Caltech, I don’t. Yes you have to do this and I got hooked again, I said Wow, this is really exciting stuff, but I thought it was not possible for me to go to a school like that, because tuition and things and we didn’t have any money and I had no idea that many of the good schools support poor students, so I was very fortunate again. They were recruiting for the freshmen who fail and to replace the sophomore class and you just take the finals from the freshman year and I did well and I got in. Then I found myself in an environment that I had never imagined where people were really scientists, they were thinking about original questions and how you get answers to them and I just didn’t even know that world existed.

You’ve highlighted the importance of the teacher in identifying you, spurring you on and finding the right connections. Do you think that in the US there are more science teachers like that than there were in your day or is there a paucity as there is in many countries now?

Leland Hartwell: I really don’t know, I don’t have much feel for the quality of science teachers in high school. I think that the general impression is the quality’s not very high, it’s often considered a default career.

Which has to be wrong it has to be said.

Leland Hartwell: Yes, I mean for several reasons, one is, and now I realise that you those people have a huge influence and that’s really important but on the other hand we just don’t pay them enough and so it’s not considered a very lucrative career, but teachers should really be paid a lot more than they are.

Anyway, you found yourself at Caltech in this lovely environment and you quite quickly decided that you were going to move towards biology from the physical sciences. What catalysed that change?

Leland Hartwell: That was again the influence of an individual. It was a very interesting time, it was around 1957 or so, it was only three or four years after DNA structure was described. I entered as a physics major and I took a biology course as an extra credit sort of thing and the teacher for that course was James Bonner who was an early molecular biologist, a plant biologist. He was just so excited about DNA and RNA and proteins and cell biology and stuff, you could just see that for the first time there was an opportunity to understand life at a molecular level and that was just so incredibly exciting that I had no choice. It’s funny because at the time I thought I was giving up my career. There weren’t careers really in biology at that time, it was a brand-new science, molecular biology, there were good careers for physicists but it’s funny by the time I got out of graduate school the physicists couldn’t get jobs and biologists were in great demand so you can never predict those things.

Your conversation sounds very similar to Jim Watson’s description of his reading Schrödinger’s What is life and deciding that the problem to solve was exactly that.

Leland Hartwell: Yes.

It’s the same experience. You turned again quickly to cell regulation, what in particular attracted you to that?

Leland Hartwell: I’d had two good experiences in all getting a glimpse of how good science was done in molecular biology. One was when I was an undergraduate with Bob Edgar who was in Max Delbrück’s group and there I was fortunate enough to do bacteria phage genetics and be close to the work that Bob Edgar was doing in terms of studying the morphogenesis of phage and using genetics to take apart the whole morphogenetic pathway of the virus and that was terribly exciting.

You saw that genetics offered a part into studying cell growth and regulation.

Leland Hartwell: Basically what they were doing was they discovered this class of mutants that were called amber mutants that would grow on one bacterium but not in another and of course it ended up into the nonsense suppression, but what it meant was that you could find mutations in essential genes because they would be suppressed in one strain and allowed to grow and then in the other strain you could see what the consequences were. He was collaborating with Kellenberger, an electron microscopist, and they would look in the bacteria where the virus couldn’t grow and look just what they’d see and what they found was that different mutants were blocked at different stage and making the virus, so some would make heads and no tails and others would make tails but no heads and all kinds of things. They were so able to construct this pathway for how this very complicated little virus was put together and all the genes that contributed to it, 50 year of genes. The power of that was just incredible and it was very simple – it was just isolating mutants and looking at them – it’s very simple, but the power was enormous. That was a strong influence for me and then as a graduate student with Boris Magasanik at MIT I studied gene regulation and had a window on the Jacob Monod world of lac operon. that was also very influential – how genetics was able to take a part gene regulation.

When I chose to become a post doc, I knew my influence at Caltech had taught me that you know, you want to pick a big problem, you want to pick something that’s obvious so the next big frontier to me seems to be cell division and the laboratory that seemed to be doing the most interesting work was Renato Dulbecco at the Salk Institute. I went to work with Renato and he was working with animal cells and tissue culture and looking at viruses and that was kind of a fun. I was only there about a year and a half but I was seen to be in a hurry, because I only spent three years in graduate school and I spent a year and a half at my post doc, but during that time we did some sort of bread and butter experiments in terms of how viruses stimulate cellular DNA synthesis. It was important for thinking about cancer but what was important for me was I did a series of projects just like I like the graduate students to do, a series of projects trying to get a handle on something fundamental in cell biology that I could explore. I had exactly that experience of three projects that I thought were a good idea, I took them to the point where I could show they were not interesting and at that point I left and took a job at UC Irvine and I was quite frustrated, I really didn’t know what I was going to do because I had seen the power of genetics in viruses and gene regulation and now I was working with animal cells and there was no possibility of doing genetics in human cells.

Just to stop you a second. It’s interesting that you got a job at UC Irvine on the strength of three post doc projects that hadn’t really got anywhere, you’d taken them to the point of …

Leland Hartwell: As I said we did some bread and butter work too, so we had some good publications as well.

All in 1,5 years, that seems to be a in hurry.

Leland Hartwell: It was an intense time was one. I was expressing my frustration one day, I’d gotten a grant to work on animal cells although I didn’t really want to and while I was waiting for equipment to come in and things I spent time in the library and I was talking to one of my colleagues and expressing this issue about you really need to do genetics to study things in a fundamental way and he said Why don’t you work with some model organism. It was just like somebody flipped a light on and this was Dan Wulff who had also worked in the Delbrück group and had similar experiments, work of lambda phage. I just went to the library intensely looking for … I wanted to study eukaryotic cell so was there a eukaryotic cell where you could do good genetics and that lead me to yeast, budding yeast and just rolled up my sleeves and tried it. But I never had any experience working with yeast.

Did you have any worries that it wouldn’t actually be applicable to higher organisms?

Leland Hartwell: Sure. I had no certainty that it would be and it’s really funny, I think that experience has happened over and over and over again in biology, where you know the genetic code is universal in protein synthesis but cell division, that might have evolved in many different ways and of course it didn’t and other areas of cell biology over and over again we have been uncertain and found that things are universal.

Roger Kornberg’s prize last year for instance, in chemistry, where he had been working on yeast without any guarantee that it was going to be applicable.

Leland Hartwell: Yes, so it just turns out that all of that basic machinery evolved long before everything diverged and it’s all really the same stuff, so that was fortunate because I didn’t know whether that would be true or not.

In all of your studies subsequently you’ve been cataloguing vast numbers of players in cell cycle control, and the picture we have of the cell becomes more and more complicated. Are we still in a phase, do you think, of cataloguing the players that are involved in cellular regulation?

Leland Hartwell: Yes we are, we’re still in a stage of cataloguing players in all aspects of cell biology and I think that will continue for some time because it’s very very complicated, everything is very very complicated and takes hundreds of different proteins involved in processes many of which are not essential but increase the fidelity, and the accuracy, efficiency and the dynamic range and the robustness, there’s just incredible complexity in any cellular process. In fact I think that’s the profound thing we’re at now is, I don’t think it really matters whether we decide to focus our attention on the hundred known players in a process or whether we continue and find the 300 that are involved in it. The real question now is how do all these pieces work together and I think that requires a different approach to biology. We only have two approaches to biology really, the cell biology, one is you take something away by genetics or some other trick and see what happens or you get the complex process to work in some /- – -/ and then you try to purify the pieces to them and put them back together and both are very very primitive approaches.

But they’re both quite isolationist approaches looking at individual components very much.

Leland Hartwell: Yes, the biochemical one starts, they both have their advantages, the genetic one at least, things are working in the cell so they’re working right. The biochemical approach you got the complexity of the whole /- – -/ there and you’re dealing with the system rather than an isolated component, but anyway they’re both very very primitive approaches and they’re not the kind of approaches that a physicist would take with a complex system. There’s a new era in cell biology that we’re just beginning to see the beginnings of where you need to be able to monitor the behaviour of the system under perturbation and understand the dynamic aspects of it which may involve reporters at different stages in the process and seeing how they come on and go off and various kinds of things like, neurophysiologist study pathways but I mean I think the critical thing about biology that goes way beyond understand what the parts do is just the enormous complexity.

It may be a silly point to make but do you think that in some ways the approach to cell biology is conditioned by the way that cell biological pathways are always described which is this element acts with this element acts with this element, it’s basically elements acting in space whereas presumably what we actually face in a cell is an enormous concentration of things barging past each other competing for space, trying to find each other. It’s a much denser picture than we’re used to looking at when we look at cell biology text books.

Leland Hartwell: It’s hard to imagine that things move around in there it’s so concentrated. If you’ve seen diagrams of people who have actually portrayed the density of proteins in a cell and the DNA, I mean the DNA is this compact thing that’s a thousand times more longer than the cell and revolving at this enormous speed to replicate and it’s just unbelievable that these things occur.

But still if you study cell biology that’s not the picture you get probably, the picture you get is of isolated elements and it needs a great experience to reach the point of really having a mental picture of what it must be like.

Leland Hartwell: I think that will only come by getting things that report dynamically in real time from the cell and studying the cell in all its complexity and dynamics and real time.

Where will those reporter systems come from, which disciplines are needed to enter cell biology in order to give us those tools?

Leland Hartwell: Really getting beyond my capability but fluorescents crunching and things where you can see proteins in a rack or proteins fold and unfold, probably things that you know give photons off when things interact and I think it’s a real problem more for chemists than for anyone else.

In terms of systems biology, which is a growing discipline, do you think that that’s taking an appropriate approach to studying cell biology?

Leland Hartwell: I think systems biology is trying to deal with the complexity so sure, but that’s what we have to do but applying a name to it doesn’t really solve it. One aspect of systems biology is trying to catalogue all the components that’s got to start there, that’s good, but I think a real systems approach has got to be in real time in the real situation. One aspect of systems biology is simulation and mathematical modelling and that’s going to be a very powerful approach to these things too because as you say the concentrations in various things, we got to model these things because they’re not intuitive to us.

Yes, and the dynamic nature of things has only been hinted at not for … You’re currently director and you have been for some time at the Fred Hutchinson Cancer Research Centre, what do you feel holds out the most hope for cancer research in the current environment.

Leland Hartwell: I think the reason I went to the Cancer Centre about ten years ago was because I was impressed with the accumulation of knowledge and cell biology, the incredible amount of detail we have, even though we still have a long way to go. There is a lot of detail and it seems to be having a relatively minor impact in medicine and why, that’s what was kind of motivating me. There’s a lot of things to say about the question you asked, but one thing that’s very impressive about cancer is that almost everybody we cure is because we detect cancer early and almost everybody whose cancer is detected late dies of their disease and that’s been true for as long as surgery and radiation has been applied to the cancer patient. The impact of therapeutics has been relatively small and the hope of curing late stage disease with the right drug remains a dream, an unfulfilled dream despite billions and billions of dollars having been spent trying to solve the problem.

Sorry, I didn’t mean to interrupt but I was going to ask, maybe you’re about to address it, do you think that’s mis-spent money do you think that the money should be actually re-directed?

Leland Hartwell: Some of it should be re-directed or some people should be taking a different approach. The reason that that approach continues to be used even though it’s largely unsuccessful is because it’s financially rewarding. New cancer drugs cost 30-100,000 dollars a year per patient even though they may extend life a few months, so it’s lucrative, but that doesn’t mean it’s really solving problems. Anyway, one obvious approach is to try to detect disease earlier and that’s been effective in a number of cancers and cervical cancer and colon cancer to some extent and breast cancer to some extent and prostate cancer, so there’s good reason to think that it is a valid approach and there’s just not very much investment in trying to detect cancers earlier. That’s where I think at least NIH and the National Cancer Institute should be spending its money rather than things that tend to support the pharmaceutical industry. Somebody ought to be working on early detection but that idea has really lead me to a broader concept about medicine in general and what I think medicine really needs to be much more effective is just better diagnostics and I think of it in a very simple way which is that there are a number of questions you need to know about any disease. Who’s at risk for it, what is the risk, does a person have disease, which disease is it, what stage is it, what therapeutics that respond to, these are all diagnostic questions. We’re seeing the impact of molecular diagnostics primarily in cancer at the DNA level because tumours have DNA changes and you can sample the tumour and find out that it has certain DNA changes and that can distinguish it from cancers that look similar to it and is becoming quite a powerful approach to cancer management. But we have to go a lot further, we have to get beyond DNA, we have to get the protein diagnostics and combine those with molecularly targeted imaging and blood tests and various kinds of things, and I just think this field has enormous potential but again there’s very little investment in it.

What about the medical community, presumably that are highly supportive, but are doctors properly trained to take full advantage of what could be done?

Leland Hartwell: They’re not because the science hasn’t provided them with the tools so they haven’t been trained and they don’t … We have very very ineffective diagnostics for most medical problems and it’s true of infectious diseases, it’s true of any disease you look into. I was surprised, I thought infectious diseases could be easily diagnosed by the nuclei acids or something, but it turns out that if you look at tuberculosis or malaria or any of these kinds of things, they have the complexity that cancer has, there’s stages of the disease, people respond differently, people respond differently to therapeutics and so they have the same problem of monitoring the patient and individualising the approach that we have in any disease. I think this is the big frontier in medicine and in concept it’s just very very simple but nobody I think has really said this is exciting, this is where we can really revolutionise medicine.

That was going to be my last question, how do you push that agenda to increase diagnostic development, diagnostic use?

Leland Hartwell: I think what’s needed is to show it can work and I’ve been working at various levels to try to encourage that both at my own institution by recruiting people who are committed to that, raising funds for it from foundations and stuff, developing partnerships with other institutions. We have an international consortium of bio-marker groups throughout Asia and other countries trying to develop paradigms for how you do this in a team science sort of way, it’s not an individual laboratory thing, and the field is progressing. I’m very excited about the developments in the last year or so. I’ve worked with the National Cancer Institute to encourage the funding for the field and they’ve put out a couple of programmes for about 120 million dollars or so and the groups that are being funded by those programmes have made some real breakthroughs in the last year. I think within the next couple of years we’re going to see a lot of useful bio markers being found but then there’s still big problems and it’s because the economic model for validating and commercialising those is not adequate and now that I can see that field developing, I’m trying to work on a different model for validating these bio markers because at the current time things are being introduced into patient care, the nucleic acid markers are being introduced into patient care through in the US through clear approval. It’s a process by which the CMS that funds medicare and medicade approves a laboratory to do a test, reproducibly and that allows you to use that test in that one laboratory but there’s no requirement for validating it for any particular use, for knowing what information it’s providing and there’s something like 7,000 genetic tests now being performed on patients based upon this clear approval process where nobody knows what information you’re getting from that test and so that’s going to create 10,000 PSAs and that’s a disaster for medicine.

It’s just confusion.

Leland Hartwell: Yes, what we need is a model whereby a bio marker for disease becomes validated during its implementation and I imagine an irradiative and very co-operative process whereby a laboratory that is non-profit but does very high through-put, high quality tests, partners with the health care system and I think the motivation for these partnerships will be not only can we improve patient outcome, but we can reduce your costs.

And that has to be the underlying point.

Leland Hartwell: Everybody’s course very concerned about the costs of medicine, nobody’s offering any solution for that. I think there is a solution, the solution is to have better diagnostics so you can catch people earlier, you can treat them more effectively you can change the treatment if it’s not working, you can avoid treating people who aren’t going to respond with expensive treatment. I think that is the road to controlling costs in medicine and if we can partner with a medical system and it’s probably not the US, it’s probably countries where you have a single payer and work within the system where there are clinicians and the payer and the regulators and various people around the table at the very beginning, and we decide ok, what are the performance criteria about this test needs to meet before the clinicians will start using it and the payer will start paying for it and we work toward that goal.

Seems very logical. Are you advanced in these discussions with any particular other country?

Leland Hartwell: We’re at the point right now where I think we’re close to having the non-profit laboratory set up and some foundations to support it and as soon as that’s in place then I’m going to go out to different countries and see if we can build some relationships.

A last thought, does it matter whether you understand what the bio marker is actually telling you?

Leland Hartwell: It’s obviously better if you know what you’re measuring and why it’s there because then you’ll understand something about where it’s not reliable, but at first it’s got to be just empirical, does it correlate with disease or not and how informative is that, what’s the rate of false positives and the rate of false negatives and those kinds of things. You need very very good clinical samples, very high quality controls that are well matched to the patient material to be able to answer those questions, but even once you answer that question and it looks like something is useful, there’s all sorts of confounding diseases for every single disease that you don’t necessarily want to be detecting, so the more you would know about what the actual biology is that the marker’s revealing the more you will understand where it’s likely to be mis-informing.

More information is certainly better of course. Thank you very much indeed Lee Hartwell for spending time with us, that was fascinating, thank you.

Leland Hartwell: My pleasure.

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