The single most important decision of a PHD student in (pure) mathematics is undoubtedly the choice of research in their thesis work. Usually to get a PHD, one must prove at least one new result. We will refer to the achievement of this situation as ‘solving a problem’. Thus, we may adapt the ‘problem solver’ (see here) view that a PHD is centered around solving a thesis problem.

I have made the following comments in person to many people, but I thought I would record them here as well.

When selecting a thesis problem, there are many factors to be considered, some of them quite deleterious. Firstly, mathematics is, contrary to popular belief, a social endeavor. Mathematicians do not work in isolation. As the recent controversy involving Shinichi Mochizuki and his purported proof of the *abc*-conjecture has shown, a problem is not solved and a result not proven until there is consensus among the mathematical community that it is. Therefore, progress or results that are not engaged with the mathematical community basically do not exist; just like the old paradigm involving trees falling in the woods. Thus one must ensure that their work is in sync with the current mathematical culture. One should therefore not choose a problem that is so far off in the fringes that few, if anybody, is aware of its existence and fewer still have any vested interest in whether it is resolved or not.

However, one should not pick something that is too hot or attractive, relative to its difficulty. Perhaps the best example of this would be the bounded gaps between primes problem. Prior to May 2013, the problem was considered intractable, and few people dedicated any amount of time to solving it. However when Yitang Zhang announced that he had proved that there exist infinitely many pairs of consecutive primes that differ by no more than 70 million, he sent shock waves around the mathematical world. Soon there was a flurry of results improving upon Zhang’s work in various ways. It would have been an extraordinarily bad idea to choose any results directly related to Zhang’s work as a thesis problem. There were literally dozens of top level experts around the world working on this topic, and the probability that your result will be scooped is very high. Thus, one must pick a problem that is either not a very obvious one to ask but is nonetheless interesting, or one that is interesting but not so interesting that it will attract the attention of many experts.

The final, and perhaps most subtle point, is that one should not pick a problem that is conducive to an ad-hoc solution that does not generalize. The best example of this is perhaps the so-called ‘elementary’ proof of the prime number theorem. In this case, while it was extraordinary that the prime number theorem, originally proved using arguments from complex analysis, could be proved in an elementary way, the proof fell drastically short of expectations. In particular, it was widely expected that an elementary proof of the prime number theorem would shed light on the distribution of primes and perhaps even pave the way to proving the Riemann hypothesis. The elementary proof of the prime number theorem did no such thing and to this day the technique remains restricted to only being able to prove the prime number theorem. One does not want a thesis problem like this. Instead, ideally during the course of solving one’s thesis problem, one discovers that the same techniques and machinery can be applied to a plethora of other problems and thus pump out a consistent stream of papers after and establish a solid research program. Whether or not this would be the case is extremely difficulty to predict before one actually attempts to solve the problem seriously.

Usually as a new PHD student who has limited understanding of your subject area and have limited perspective on the landscape of your research domain, it is extremely important to find an advisor who does have the right expertise and perspective. Even then it is a very delicate process to select a thesis problem which you would be expected to work on for several years.

Haoran TangNice post, Stanley! This is invaluable advice. Can I share it in renren.com with my friends?

prayersontestsPost authorOf course!