A few weeks ago, a female biology professor from Berkeley gave a talk at Tsinghua as part of a women-in-science series. During the question period, a student asked how to choose a research topic. You have a choice of labs; which should you choose? You have a choice of research questions; which should you choose? An excellent question: Every young scientist wonders about this.
The speaker’s answer: Believe in yourself. Huh? This came from her personal history. When she was a grad student (at Berkeley) she proposed a certain line of research to her advisor. Her advisor said it was a bad idea. She switched to Harvard and pursued her idea there. It paid off. A sign of her success is that her lab gets $1 million/year in grants.
I wasn’t there. The friend who told me the professor’s unhelpful answer asked how I would answer the same question. During graduate school, I thought a lot about it — about how to do research that anyone will care about in fifty years. I can answer it only for experimental psychology.
First，invent a new method or study a large puzzling experimental effect. With either one you can generate a steady steam of publications. Inventing a new method mean inventing a better way — usually, a faster way — of measuring something important. You can then apply your new method all over the place. With a large experimental effect you can vary all sorts of things and narrow in on an explanation. As a grad student, I took the first route: I used a new way of studying animal time discrimination. I didn’t invent it but its inventor hadn’t seen its value. An example of the second route is the career of John Garcia. In graduate school, he discovered that making rats sick after eating a new flavor caused them to dislike the flavor. The sickness could come hours after the flavor. Garcia made a whole career out of doing variations on this.
Second, take advantage of whatever is unusual about you. If you are unusually interested in X, study X. I differed in two ways from most experimental psychologists: I was better at math, and I cared more about writing. Taking advantage of this, I spent a lot of time on data analysis and writing. Both paid off. I suppose my paper were better written than necessary but the time spent on writing paid off because I got good ideas while writing.
Third, collect a rich data set. New experimental effects are enormously important — if you manage to find one you can spend the rest of your career studying it — but are also very difficult to find. You can’t do experiments whose main purpose is to look for them. The chances of success are too low. To find them, you set up your research so that a conventional experiment has the possibility of finding them. For that you need a rich data set — a data set with many factors and many levels of each factor, ideally. The new way of studying timing that I used provided a rich data set. Quite soon this led to discovering a new effect when some of the data changed in a surprising way.
“Read a bit of Medawar” would have been more helpful than “Believe in yourself”.
I’m afraid that my first response would be to try to dissuade them from a *career* in science (which hardly exists now, and will be even rarer by the time that they are dvanced in their research program) – and instead to do real science as an amateur hobby, instead of becoming a manager or technician merely pretending to do science as a paid job.
I agree with Bruce. But if someone insists on going into science anyway, my advice would be to find a mentor who has a reputation of being good to his or her graduate students (i.e., paying attention to them and ensuring that they finish their PhDs in a reasonable amount of time). Finding an interesting research topic is all very well and good, but if you can’t get out of grad school, the point becomes moot.