Recently I interviewed two job candidates for an assistant professor position at Tsinghua. I asked both of them: “Why did you decide to study this?” (this = their field of research). One had no answer at all. The other had an answer that didn’t make sense. I didn’t mean it as a tough question. If they had said “because that’s what they were doing where I got a postdoc” I would have been perfectly happy. If that were the answer, I might have asked “why does your advisor study it?” — to which “I don’t know” would have been perfectly acceptable. Of course, there are better answers.
When I was a graduate student, I read Adventures of a Mathematician by Stanislaw Ulam (a very good well-written book). One of the book’s comments impressed me: That John Von Neumann was able to distinguish the main lines of growth of the tree of mathematics from the branches. My research was about how rats measure time. The relevance to big questions in the psychology of learning wasn’t obvious. I wondered: Am I studying something important? Or something that will be irrelevant in twenty years? My advisor didn’t seem to have thought about this.
When I interviewed for jobs at various universities, no one asked me why do you study this? But it was still a question worth answering. As a grad student I had no choice. But eventually I would have a choice: I could continue to study how rats measure time. Or I could study something else. (Eventually I did change — to studying what controls variation in behavior.)
Here’s what I would say now about how to choose a research topic.
What’s best is a new method. If you can use a new method to answer questions in your field, do that. The cheaper, easier and more available the method, the better. As a graduate student, I developed a new way to study how rats measure time, which I called the peak procedure. It made it easier to determine if an experimental treatment affected an animal’s internal clock.
What’s second best is a new experimental effect. Discovering a new way to change something of interest. The bigger, cheaper, newer, and more surprising the effect, the better. Using the peak procedure, my colleagues and I discovered a large and surprising effect (at a certain time during the peak procedure, the variability of bar-press duration — how long a rat holds down the bar when pressing it — became much larger). When I first saw the result, I assumed it was due to a software mistake. It turned out to be a window in what controls the variability of behavior — an easy way of studying that. In that sense it was also a new method.
I don’t know if the two job candidates I interviewed were doing either of these two things. Maybe not. My broader point is that if you don’t have a good understanding of how to choose a research topic you will have to retreat to studying something simply because others are studying it. Which is exactly the wrong thing to do if you want to be an innovator and a leader.