I don't think anyone finds what I'm working on interesting. What should I do?

Question

I'm in math but not currently in academia (completed PhD). I had to leave and I'm trying to get back. Recently I've been working on some small problems that I made up myself from reading some papers. But it's not part of any sort of larger program or is related to stuff that people work on. So, I am worried that when people look at my research statement, etc., nobody will find it interesting and will pick someone else who works on trendier things, or that is part of a bigger research group.

One person told me that I should continue working on what I find interesting, because otherwise I would be "pandering." That's bad because that sort of defeats the purpose of doing mathematics, which should be done for intrinsic reasons. But wouldn't that lead to my applications being turned down? Should I think about who might find my work interesting?

Answer 1

Two ideas:

First, it is fairly common for mathematicians to work on things of interest to only a few people. When I completed my dissertation (previous century) it was quite interesting but of interest, really, to only half a dozen people worldwide and I knew most of them. Don't let that be a concern. You can even get things published in good journals, as the main results of the dissertation were. Math is very balkanized and interesting things can pop up anywhere. For some, the personal rewards are enough.

Second, academia is a big place. it might be very hard to get hired at an R1 but there are lots of satisfying careers at other universities and colleges, including liberal arts colleges, all of which are likely to have a math department. While research is less important (than teaching) there, it still gives an opportunity to do it and if you keep up a circle of collaborators you can succeed. You can also move up the food chain if you are able to publish.

So, look at all the possibilities and cast a wide net.

Answer 2

There isn't a right or wrong decision what you should work on. It's entirely your decision, taking into account both your own passions and interests, and the likely rewards of succeeding at solving different types of problems. It's certainly the case that not all problems are created equal in how highly they are regarded by the mathematical community, and how much solving them will advance your career in a practical sense.

In any case, you might consider that if you decide to do a bit of "pandering" to advance your career, you will be in pretty good company. Gauss was twenty-four and already well-known for his amazing discoveries in number theory when he decided to work on an applied problem in astronomy: calculating the orbit of the dwarf planet Ceres, which had been discovered at the beginning of 1801 and observed for a brief period but then could not be located again by astronomers. The problem of finding Ceres became quite a trendy topic that attracted the attention of the scientific community of the day. Drawn by the opportunity and interest generated by this problem, Gauss attacked it and, through heavy calculations combined with ingenious methods he had developed, was able to calculate the orbit of Ceres and predict its future position from the recorded observations. This was a stunning success: astronomers pointed their telescopes towards the positions Gauss predicted and swiftly located Ceres.

In chapter 14 of his classic book "Men of Mathematics: The Lives and Achievements of the Great Mathematicians from Zeno to Poincaré", author Eric Temple Bell describes Gauss's motivations for working on the problem of the orbit of Ceres:

His friends and his father, too, were impatient with the young Gauss for not finding some lucrative position now that the Duke had educated him and, having no conception of the nature of the work which made the young man a silent recluse, thought him deranged. Now at the dawn of the new century the opportunity which Gauss had lacked was thrust at him.

[...]

Why not indulge his dear vice, calculate as he had never calculated before, produce the difficult orbit to the sincere delight and wonderment of the dictators of mathematical fashion and thus make it possible, a year hence, for patient astronomers to rediscover Ceres in the place where the Newtonian law of gravitation decreed that she must be found—if the law were indeed a law of nature? Why not do all this, turn his back on the insubstantial vision of Archimedes and forget his own unsurpassed discoveries which lay waiting for development in his diary? Why not, in short, be popular? The Duke's generosity, always ungrudged, had nevertheless wounded the young man's pride in his most secret place; honor, recognition, acceptance as a "great" mathematician in the fashion of the time with its probable sequel of financial independence—all these were now within his easy reach. Gauss, the mathematical god of all time, stretched forth his hand and plucked the Dead Sea fruits of a cheap fame in his own young generation.

Bell proceeds to describe the rewards that Gauss reaped from his feat:

Recognition came with spectacular promptness after the rediscovery of Ceres. Laplace hailed the young mathematician at once as an equal and presently as a superior. Some time later when the Baron Alexander von Humboldt (1769-1859), the famous traveller and amateur of the sciences, asked Laplace who was the greatest mathematician in Germany, Laplace replied "Pfaff." "But what about Gauss?" the astonished Von Humboldt asked, as he was backing Gauss for the position of director at the Göttingen observatory. "Oh," said Laplace, "Gauss is the greatest mathematician in the world."

Of course, Gauss is only one of numerous mathematicians whose choices of what to work on were influenced by considerations of career success. Was Gauss's decision to work on an applied problem really "pandering"? Did it "defeat the purpose of doing mathematics"? I'll let you judge for yourself.

Answer 3

One person told me that I should continue working on what I find interesting, because otherwise I would be "pandering."

I don't agree with this advice. At least, not for young researchers. The accumulated expertise of the mathematics research community is valuable, and you should learn from it as much as you can in the early part of your career. A big part of that expertise is a "nose" for good problems to work on, and this takes time to develop. It usually develops a few years later than the ability to solve research problems that a mentor helped you select.

I don't know much about your situation, but if you're still at the stage of asking for general advice about what to work on, then you should try to get advice that's as tailored and specific as possible, and get it from as qualified of an expert as possible. Which usually means entering into some kind of mentorship arrangement (formal or informal). On a practical level, it will be very hard to get back into academia without at least one well-established person in your corner.

Eventually, once you've reached a certain level of expertise, you can strike out on your own if you want to do that, and you'll be able to judge the worth of your ideas for yourself. But it's difficult to gain that expertise working in isolation on your own questions.

Answer 4

When you leave academia, you need to stay in touch with academia and perform up-to-date research. If you can publish from time to time, it should be enough to demonstrate a potential employer that your are capable to research on your own.
I assume you apply to open positions. There you won't do your own research, but follow the ideas of a PI, do work which was promised for grant money, or help with the problem of your new colleagues.

You should clarify what your strategy is to get back to academia. I suspect that your actual problem are your unsuccessful applications. Probably you have to post a new question addressing this issue.