Early in my mathematical life, my selection process was largely passive, in the sense that more experienced mathematicians would put problems in front of me, and the only decision I made was whether or not to work on them. My first published paper was born on USENET. Chris Long posed some question about Fibonacci numbers that I think he had discovered empirically. I solved it and it turned out to be interesting enough to be published in the Fibonacci Quarterly. Obviously, there was a large amount of randomness involved here. I did not already know Chris Long, and I was not even intentionally looking for a problem to solve and publish, so for me to stumble across his problem and solve it was quite serendipitous.

Soon afterwards I participated in Joe Gallian's REU. There again, Gallian presented me with problems to try to solve. At least in this case, the arrangement was formal—I was there to try to publish a paper, and he was there to try to find a problem that I could solve. However, I was still largely passively receiving problems rather than actively seeking them out. This pattern continued through my Ph.D. degree; my advisor suggested various problems and I eventually obtained enough results for a thesis.

At some point, the dynamic began to change somewhat. The first reason was that in the process of getting my degrees, I was learning more and more math, and developing a sense of what questions were important and what questions were tractable. Thus I was developing the ability to ask my own questions, instead of having to rely on an external source to feed them to me. The second reason was that I was getting exposed to more and more open problems, just by listening to talks and reading books and papers. Gian-Carlo Rota has said that the trick to becoming a genius is to keep a short list of difficult open problems in your pocket at all times, and every time you learn a new mathematical technique, to try it on every problem in your list. If you ever get a hit, people will say, "How did he ever think to use that technique on that problem? He's a genius!" Over the years, a few problems have attached themselves to me like a burr, usually because I found them fascinating and thought I might be able to solve them but couldn't. I have several papers of this type, where I finally managed to make progress on a question that had been nagging at me for years.

I think that the type of progression I have just described is fairly typical. Initially, most people have to be told what to work on. As you learn more, you are able to generate new questions on your own, and you accumulate other people's open problems that you find attractive.

As a final comment, I would say that there can be external factors that dictate to some extent what you work on. When I was a postdoc in academia, I felt pressure to publish lots of papers, so I tended to stick to topics that I knew a lot about. To publish a paper, one needs to find that elusive boundary between the trivially easy and impossibly hard, and if one ventures into unfamiliar territory, that boundary can be very difficult to locate. I think that this effect is stronger than many people are willing to admit. A lot of people choose to work on a problem simply because it's in familiar territory and they are pretty sure that they can make progress on it. I personally am fortunate enough to be in a position where this kind of pressure is low and I have considerable freedom to try new areas of interest even if it will take some time before I can make progress. So I am guided more by what I find interesting than by what I feel I "have to" work on in order to keep publishing.