A doctoral program or postdoctoral fellowship is an opportunity to learn to think better as a scientist, gain an understanding of the open questions in a field of science, apply existing skills to new problems, and acquire new skills, whether quantitative, experimental, or otherwise. Less obviously, but at least as importantly, it is a chance to gain a sense of “taste” in science – a sense for what is a good scientific problem, what is an important question to answer for practical purposes, what is an elegant solution to a problem, how to be a good critic of one’s own (and others’) results, and when to consider a question solved.
As in many matters of taste, thoughtful people can disagree about what is important or interesting. Scientific progress depends on the joint efforts of many different “styles” of scientists — experimentalists and theorists, analysts and methodologists, big-picture thinkers and meticulous workers-out of details, and the like. Nonetheless, it pays to think carefully about what project to work on. Any but the most trivial project will be difficult and time-consuming, so it only makes sense to pick the most interesting and/or important project one can find. As Sir Peter Medawar memorably puts it in his excellent Advice to a Young Scientist (p. 13),
It can be said with complete confidence that any scientist of any age who wants to make important discoveries must study important problems. Dull or piffling problems yield dull or piffling answers. It is not enough that a problem should be “interesting” – almost any problem is interesting if it is studied in enough depth.
As an example of research work not worth doing Lord Zuckerman invented the cruelly apt but not ridiculously far-fetched example of a young zoology graduate who has decided to try to find out why 36 percent of sea urchin eggs have a tiny little black spot on them. This is not an important problem; such a graduate student will be lucky if this work commands the attention or interest of anyone except perhaps the poor fellow next door who is trying to find out why 64 percent of sea urchin eggs do not have a little black spot on them.
Indeed, many of the ideas in this note are inspired by Medawar’s book, which is quick and excellent reading for anyone in science. Other good references on this topic are the curmudgeonly “Some Modest Advice for Graduate Students” by Steve Stearns (aimed at students in ecology and evolution, but relevant in many disciplines), and the “acynical” reply by his colleague Ray Huey. More recent excellent pieces by Jonathan Yewdell are here and here.
Given that scientific tastes differ, even the most outstanding research groups will be a good fit for some highly talented students or postdocs and a poor fit for others. The same goes for the fit between graduate programs and students.
How can you assess whether you would fit in well to a particular research group? The best place to start is by reading papers from that research group. If at the end of reading a paper you think, “I wish I had done that work,” it’s a good sign. If you can explain convincingly to a neutral third party why the work is exciting, so much the better. If the paper is written by a trainee at the level for which you are applying (e.g. a doctoral student), it’s an even better sign. On the other hand, if you can’t understand why the papers you have read from the group are either scientifically interesting, or practically important, or elegant in their solution to a hard problem, then you probably won’t enjoy being a part of the group.
Two points to emphasize: if you are a scientist, there should be many scientific papers whose results you find interesting. Only a subset of these report work you wish you had done yourself. That’s’ a more stringent requirement — not only is the outcome exciting, but the process of discovery is one you would have liked to participate in. Look for labs where the work itself excites you, not only the results.
Second, note that the emphasis here is on research findings and good ideas, not on the technical approaches. Doctoral and postdoctoral studies are a time to learn technical skills, but this should be possible at almost any high-quality institution. Except in very specialized cases, the range of techniques on offer should not be a major criterion for choosing where to be a student or postdoc. Indeed, in many fields the techniques that are novel now will be out of date within a few years. Moreover, for very many questions, a mixture of techniques – for example, observational studies of humans and mechanistic studies in animals – will be required to get a firm answer, and it’s far better to learn how to adapt techniques to answer a question, rather than to search for questions susceptible to a particular technique. Choice of a program or research group should hinge on whether you find exciting the ways in which they apply their techniques, and whether you expect that in that group, you will learn to think more clearly and creatively as a scientist.
Many prospective students (and sometimes also postdocs), mention that they hope to “keep their options open” during their training. I think this is a fallacy. More precisely, if you make this your main goal and try to learn a little of everything without delving into some topic to make yourself an expert, the result will be to reduce, rather than preserve or expand, your opportunities. This is true for several reasons. For one thing, taking classes and learning skills is far more rewarding – and you’ll remember what you learned much better – if you have a concrete problem in mind that you are trying to solve with the skills you’re learning. For another, having taken a lot of classes in different areas will not do much to improve your appeal to prospective collaborators/employers/advisors later on. Your future “marketability,” to use a crass term, will be greater if – at whatever stage you now are — you find a problem that excites you, learn what you need to address it, and try to solve it. If you have done that in one field, you will find many opportunities later on to move into related fields. More importantly, you will have spent your time well in the interim, developing depth in one field and making a real contribution to knowledge in that field, hopefully having fun in the process.
For example, if you do exciting work in biostatistics, you will find yourself in demand and encounter opportunities to apply these skills in global health, or in infectious disease dynamics, or in bioinformatics. If you have made important contributions to a field study in the epidemiology of a particular infection, and you have educated yourself in the biology, population genetics, or mathematical modeling work on that infection, you will find a way to move laterally into one of these allied fields if your interests start to move in those directions. In summary, you will have more opportunities in related fields if you have focused and done one thing well, than if you have taken lots of courses and learned lots of techniques, but not done much with them.
This isn’t just my opinion. Much of the field of infectious disease dynamics has been developed by scientists trained in physics or ecology. Molecular biology didn’t exist until the ‘50s, when it was invented by physicists, chemists, and geneticists. The human genome project was developed largely by people trained before the terms “computational biology” and “bioinformatics” were even coined. All of these field-changers (and field-creaters) kept their eyes open, saw new problems that needed solving, and got themselves educated enough, on the job, to start solving them. It may feel as if “keeping options open” is about what others will think of your training – have you defined yourself as someone who can do X?. In fact, having many options is largely a state of mind — fed by curiosity and an active mind that takes in and processes information from a variety of sources – combined with an ability to think both creatively and rigorously – which will open doors in many different fields, some of them not yet even imagined!