BARCELONA, SPAIN—Many factors influence success in a science career, including hard work, tenacity, flair, and luck, and all of them have played a role in the success of Nobel laureate Tim Hunt, who today is a group leader emeritus at the Cancer Research UK London Research Institute. But in addition to these factors, Hunt, who won a share of the 2001 Nobel Prize in physiology or medicine (along with Leland Hartwell and Paul Nurse) for his discovery of cyclin, a key regulator of the cell cycle, emphasizes early independence and playfulness.
During a Postdoc Day organized in spring by the Institute for Research in Biomedicine in Barcelona, Hunt reflected on the research hurdles and milestones that led to his Nobel-winning discovery. In a followup interview with Science Careers, he shared his vision of what matters most in a scientific career and offered advice to early-career scientists on how to be successful.
The only thing I know I’m really good at is spotting little things that don’t make sense.
The following highlights from the interview were edited for brevity and clarity.
Q: After your Ph.D., you went to do a postdoc at the Albert Einstein College of Medicine in New York City to continue your work on the regulation of hemoglobin synthesis. In your talk today you said that your postdoctoral project did not yield any major results. How did you manage to keep going during those 2 or 3 years?
T. H.: I was in a rather peculiar position because after a year the boss decided to go set up a new medical school, so I was kind of left by myself. It was just me and a technician called Grace Vanderhoff, and we had to sort of make things up as we went. So I usually had two projects going, one that I did with Grace during the day and my own project, which I did at night. Gradually the night projects started to go better than the day projects. In fact, they allowed me to discover two very important things, which both came through collaborations with people from other labs. We discovered that both oxidized glutathione and double-stranded RNA were extremely inhibitory to protein synthesis in reticulocytes. So that was a Nature paper and a PNAS [Proceedings of the National Academy of Sciences] paper.
I think it was a bit easier back then to collaborate. Nowadays, people are all in their separate silos and are so specialized that it’s hard to understand what anybody else is doing but, in addition, there was this lovely atmosphere at Einstein where people were very prepared to collaborate.
We did write a paper on my daytime postdoc project, but it was not a paper I am at all proud of because it didn’t explain anything.
Q: What was your next career step?
T. H.: I returned to Cambridge to work in the Department of Biochemistry at Clare College. And this is another thing that I think was very lucky: I was able to take an independent fellowship. It paid very little—I took a five-fold cut in pay—but I found myself among friends, namely Richard Jackson and Tony Hunter. Richard had a university position, but the rest of us did not, and it was like a sort of a loose federation of graduate students and postdocs, and we could just do whatever we liked. You could teach, and we did teach, but you could always say, “bugger off” if you didn’t want to do something. This was terribly satisfactory, and we had a really lovely time.
Still, we were a bit anarchic and bumbling in a way, and I sometimes regretted that I never had any proper formal biochemical education. We all had to work everything out for ourselves. But after a while, I realized that I understood the rabbit reticulocyte lysate system much better than anybody else in the entire world, because I had made every single mistake that was possible to make and learned from them.
It strikes me that everything is much more formalized now, and I find myself reacting badly to this idea that there are skill sets you need to have, and you must pass your exams to get them. I would rather emphasize the importance of playfulness, and of making your own mistakes.
Q: What was the outcome?
T. H.: Back when I joined, my friends had just discovered that the binding of an initiator tRNA [transfer RNA] was the key for starting hemoglobin synthesis, and we fairly soon found out that all the inhibitory factors I had been studying in New York blocked this very initiation step. In particular, there was a complex between the 40S ribosomal subunit and initiator tRNA that went away when heme was missing or double-stranded RNA was present. It was very controversial to start with because we discovered that the mRNA [messenger RNA] does not instruct the ribosome what tRNA to bind, as was believed back then. Rather, the tRNA binds first to the ribosome and then instructs the ribosome where to go on the mRNA. People said, “No, this can’t be right. This complex you’re talking about, it’s an artifact.” That’s when you know you made a real discovery, when the reviewers say, “It can’t possibly be true.” The same occurred with the cyclin discovery.
Q: Would it be possible for young scientists nowadays to work as independent postdocs?
T. H.: Well, I think so. There are still these fellowships around, so it depends on the environment you find yourself in. I didn’t like the fact that everybody is supposed to be a PI [principal investigator] with grants and people under you. I really admire these people who can have a lab of a dozen or two dozen people and get the best out of all of them, but I’ve been happiest when I’ve had one or two really close collaborators. The key thing is that you must somehow get independent when you are really young, and take responsibility. I think a PI has too much responsibility. In general, it takes people out of the lab and into their offices just when they get really good at doing and designing experiments, and that’s a shame.
During those years, both Tony and I applied for jobs in Cambridge, and both of us were rejected. We published some nice papers, but it wasn’t until 1975 that we finally cracked the problem of how lack of heme or the presence of double-stranded RNA inhibited globin synthesis. In retrospect, not getting a job was the best thing that could have happened because it kept us out of teaching, which really takes too much time and energy.
It wasn’t until 1981 or 1982 that I finally got a job. My career and the careers of people I knew weren’t really careers. You kept going, but it was in a pretty wandering sort of way and a bit opportunistic. In my case, that lasted roughly 10 years.
Q: How did getting an academic position affect the way you did your research?
T. H.: That was the end really. That was why I had to start going off to America during the summer to the Marine Biological Laboratory at Woods Hole, in order to get away from everybody and do some work. Those summers were very productive, also because you were working on totally unfamiliar material that nobody else worked on. But you had all the tools that were well honed, so almost any experiment you did was going to find something new and interesting. And in this context, where students came to do little research projects instead of just learning trendy new techniques, I loved teaching.
I went to Woods Hole so as to be able to work on sea urchin eggs, as by then we had a good understanding of our reticulocyte system. I was looking for a new model to study the control of mRNA translation into protein, and back when I was a graduate student, I had heard a talk from Henry Borsook that compared protein synthesis in sea urchin eggs with hemoglobin synthesis in red cells. This led me to enter the field of developmental and cell biology, and to eventually discover cyclin as a key regulator of the cell cycle.
Q: It takes a lot of confidence to stand by your results when they are controversial. Do you have any advice for early-career scientists?
T. H.: You have to be very sure of yourself, it’s true, but you’re sure of yourself because you know the experiments are robust. Another lesson I learned very early on: Tony and I failed to do an obvious control and, as a result, made a misinterpretation. It was very irritating to be wrong about something, so ever since then, I’ve tried to think of even controls that seem completely pointless, and do them, because if you don’t, there’s going to be one that trips you up. I always tell people, “Be your own harshest critic because then nobody can hurt you.”
Q: What do you think was the key to your success?
T. H.: Identifying a good problem to work on. That’s the most difficult thing. I know a lot of scientists who are much better than I am, smarter and more able. The only thing I know I’m really good at is spotting little things that don’t make sense, like that double-stranded RNA thing, or the protein that I saw going away on the original cyclin gel, even though it wasn’t what I’d been looking for, and the dogma of the time said that proteins didn’t go away. That was a really important clue because the importance of that discovery is that you could specifically degrade a protein in cytoplasm while all the others were perfectly stable. This was not known at all, and the idea that it could be a secret of cell division was so far from people’s minds that nobody had ever suggested it.
I also think that behind it all, there was a fairly steely ambition. It’s a perfectly healthy ambition to want to win a Nobel Prize. I didn’t have this ambition exactly, but I thought, “Why wouldn’t you want to find out the most important thing you possibly could?” I was very lucky growing up when I did in Cambridge, because we were surrounded by Nobel laureates. We never felt that we were in the same league as these Sangers, Cricks, and Brenners, but you realized that even if they were Nobel laureates, you knew stuff they didn’t, and you also realized that they are an amazingly heterogeneous bunch.
In short, when people ask me, “What is the secret to success?” I always say, “Keep your eyes on the horizon but your feet on the ground, and preferably your nose to the grindstone.” In other words, you have to work.