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A lot of posts like this are from graduate students or undergraduates. I'm tenure track at a Small Liberal Arts College (SLAC) and been through a couple of postdocs, so I know what Math research is. I just think I'm bad at it.

  1. I haven't thought of any interesting questions I'd like to look into that didn't directly come from my thesis work
  2. I've been part of a couple big group projects, and every time I felt like I was sprinting just to understand the things my coauthors wrote; I didn't add any new ideas of my own.
  3. I've been part of 3 projects in the last couple of years that basically ended up with us shrugging and saying we had no ideas, and we stopped meeting about that.
  4. It's been about 3 years (in a postdoc) since I've discovered anything that I thought was neat and actually got excited about it. Even that was pretty small, and at the time I was not teaching. So when I have zero other responsibilities, I'm capable of coming up with something minor.

The comments in posts like these usually advise the writer to look up imposter syndrome and not give up. I'm not going to give up; I like research. But I think there's something more going on here than imposter syndrome. The way people start collaborating with each other feels like a mystery to me. I go to talks and I ask questions, but I don't know how to go from that into actually starting a project. And when I do join a project, I don't seem to be able to come up with any good ideas.

I feel like the calculus student that does 100 problems and gets all of them wrong. I'm going to keep trying, but I feel like I'm missing something important here.

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    Edited the title to reflect I'm at a SLAC. I know I don't have to have the highest level of research to get tenure, but it's not fun to start projects and then abandon them because I can't make any progress Oct 19, 2023 at 23:44
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    Could you say a bit more about yourself, i.e. (1) are you a pure or an applied mathematician (the cultures are frequently different), (2) how did you manage to write your dissertation? Did you have some ideas of your own or were you told by your advisor what to do on every single step no matter how small it is? My advice would depend on these factors... Oct 20, 2023 at 21:46
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    @MoisheKohan (1) pure (2) My advisor gave me some ideas but they did not tell me what to do on every single step. I do think they gave me good advice about when to keep fiddling with a problem and when to walk away, which is something I find very difficult now. I really struggle with deciding if I need more background information to attack a problem or if I haven't been thinking about it on my own hard enough/long enough (I've made mistakes in both directions...) Oct 20, 2023 at 23:52
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    Does your school or department have any faculty mentoring programs. Oct 21, 2023 at 21:17
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    @ScottSeidman I have a mentor in my department who's 70 years old and while he's very kind, he hasn't done his own research in a while. I could ask him but this question makes me feel pretty vulnerable so I'd rather not ask if the chance he has good advice is slim. Oct 22, 2023 at 3:06

9 Answers 9

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For the record: I am a pure mathematician. I never worked in a SLAC (only in reasonably large, 40-50 faculty, research oriented math departments). Nevertheless, your struggles are not at all unfamiliar. Even after 40 years of doing math research I frequently find myself "beating my head against the wall" and asking myself if I should simply spend more time working on a problem or to set it aside and work on something else. And this question has no good answer. Here are few thoughts and suggestions (in addition to the advice that you got in other answers).

Collaborations are good, but, ultimately, in pure math, it is all about you and the notepad and a pen in front of you: Either you figure things out or you do not. (Caveat: On few occasions, my collaborators have bailed me out by providing with some key ideas or proofs which I was lacking; however, this is not a representative sample since these were winners of IMOs or mathematicians with problem-solving skills at a similar level. I was very fortunate having such high-power collaborators.) So, what would I do in your situation?

  1. The idea suggested by Alexander Woo of switching to an "easier" area of math, with more "low-handing fruit" is not bad, but is easier said than done. For this, your best option is to have somebody in your current department whose research you find interesting and which is, at least, marginally, related to what you know. For instance, maybe your field is algebraic combinatorics and you have a colleague doing, say, graph theory, or studying combinatorics of convex polytopes. Or maybe you are working in geometric flows and your have a colleague working in applied parabolic PDEs. You can start a conversation by asking them to tell you more about their research. People in general like to talk to colleagues about their research. But keep this open, not suggesting from the beginning that you would like to collaborate. If such a conversation leads to a collaboration, then it should happen naturally, through shared common interests or you having some ideas/technique that your potential collaborators may find useful. Keep in mind that some things that you regard as "trivialities" and routine may come as a revelation to your colleague, simply because they were never exposed to these.

  2. Start small. This means, thinking in terms of lemmas, not theorems. Are there any loose ends from your thesis work that would be nice to sort out? Are there some small issues in papers that you have read as a student or a postdoc that deserve some elaboration? Are there any notions in your area which are poorly explained in the existing literature and are worth writing an expository paper on? (Maybe they are not even poorly explained, just there could be some audience for a more down-to-earth explanation than the one in the literature.) Are there any (even marginally) interesting examples which nobody bothered (or could not) work out in detail? While working on your thesis you, presumably, have learned some specific technique. Are there any questions (no matter how uninteresting you may find them at this point!) that can be handled by the same or a similar technique? If your work involves estimates (which is frequently the case, say, in analysis, or PDEs or in number theory), can you improve (even just a little bit) on these estimates? Will any of these lead to a publication? I have no idea and nobody does. But keep in mind that in your college there are might be some very smart undergraduate students interested in REUs. Some of what I described above may lead to a joint publication with a student, which will be good for both of you. It will not be a paper Annals or even Proceedings of the AMS but it will be a start, getting you out of the hole you find yourself in.

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    Let me make myself clear: my suggestion is to switch to something that many serious research mathematicians would regard as stamp collecting - sideline work that provides the intellectual stimulation of research (for both the OP and for their students) but does not advance the story of mathematics. The suggestion of working on graceful labellings of near caterpillars was at least somewhat serious - it's the kind of topic people in OP's position have jumped in on without background in the area or a collaborator and gotten some new publishable results. Oct 22, 2023 at 0:57
  • Reading you write that my struggles are not unfamiliar was so validating, thank you. And this is all excellent advice. Oct 22, 2023 at 3:09
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Try taking time out to just play with your field for your own enjoyment

The physicist Richard Feynman went through a similar period of "burn-out" in his research where he was not making progress on research problems. He decided to stop trying to do research work and instead just play with ideas in his field that he found personally interesting, without regard to where they would go. Here is an excerpt from his biography explaining what happened:

So I got this new attitude. Now that I am burned out and I'll never accomplish anything, I've got this nice position at the university teaching classes which I rather enjoy, and just like I read the Arabian Nights for pleasure, I'm going to play with physics, whenever I want to, without worrying about any importance whatsoever.

Within a week I was in the cafeteria and some guy, fooling around, throws a plate in the air. As the plate went up in the air I saw it wobble, and I noticed the red medallion of Cornell on the plate going around. It was pretty obvious to me that the medallion went around faster than the wobbling.

I had nothing to do, so I start to figure out the motion of the rotating plate. I discover that when the angle is very slight, the medallion rotates twice as fast as the wobble rate - two to one [Note: Feynman mis-remembers here---the factor of 2 is the other way]. It came out of a complicated equation! Then I thought, "Is there some way I can see in a more fundamental way, by looking at the forces or the dynamics, why it's two to one?"

I don't remember how I did it, but I ultimately worked out what the motion of the mass particles is, and how all the accelerations balance to make it come out two to one. I still remember going to Hans Bethe and saying, "Hey, Hans! I noticed something interesting. Here the plate goes around so, and the reason it's two to one is ..." and I showed him the accelerations.

He says, "Feynman, that's pretty interesting, but what's the importance of it? Why are you doing it?"

"Hah!" I say. "There's no importance whatsoever. I'm just doing it for the fun of it." His reaction didn't discourage me; I had made up my mind I was going to enjoy physics and do whatever I liked.

I went on to work out equations of wobbles. Then I thought about how electron orbits start to move in relativity. Then there's the Dirac Equation in electrodynamics. And then quantum electrodynamics. And before I knew it (it was a very short time) I was "playing" - working, really - with the same old problem that I loved so much, that I had stopped working on when I went to Los Alamos: my thesis-type problems; all those old-fashioned, wonderful things.

It was effortless. It was easy to play with these things. It was like uncorking a bottle: Everything flowed out effortlessly. I almost tried to resist it! There was no importance to what I was doing, but ultimately there was. The diagrams and the whole business that I got the Nobel Prize for came from that piddling around with the wobbling plate.

Now, I am not suggesting that this method will win you a Nobel prize, or even that it will bear fruitful research, as it did for Feynman. Nevertheless, one of the nice things about this approach is that it lets you go back to what you enjoyed about your discipline, which means that there is increased job satisfaction irrespective of whether there is any research benefit. Since you're not presently making any research progress, you're no worse off if this approach still yields no research progress but just lets you enjoy your job and life a bit more. It is likely that this method will at least allow you to identify some toy problems that you find interesting, which will give you something to play with to keep your brain active.

I have found this approach useful in my own research. I often get interested in problems purely for my own enjoyment and then play with them over a period of time just for fun. Sometimes this bears fruitful research but often it leads me to rediscover things that are already published. In either case it is useful to get my brain working and I've found that it tends to lead to a large number of research ideas (more than I'll ever have time to pursue). This at least nullifies the problem of having nothing interesting to research, which is a good first step.

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    I like your suggestion, but I don't know how feasible it is for the average (not wealthy nor exceptionally brilliant) person. It's difficult to find time and energy to enjoy learning a topic just because one finds it interesting, or working on problems (not related to a research project) out of curiosity. There's too much time-consuming, non-research tasks to do to afford that.
    – Amelian
    Oct 20, 2023 at 6:24
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    @Amelian The suggestion is indeed counter-intuitive, but it's precisely this decision to work on things you enjoy in the slivers of time available to you that makes the rest bearable. If something excites you, there is much you can bear. If nothing does, even the smallest chore will crush you and take up all your energy. In other words, energy levels should not be treated as zero-sum by default. My French teacher used to say that it's the laborer who benefits from poetry the most, and the older I get the more I see what he meant.
    – Qwokker
    Oct 20, 2023 at 12:53
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    I like this perspective, and I think it does address the problem of me not being able to come up with questions. I'm still a bit worried about my ability to answer those questions, but one step at a time I guess Oct 20, 2023 at 13:05
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    @vegetableRoar: In my experience, playing around with math all the time does not only help in coming up with questions - it's also extremely useful for being able to prove new results and to solve questions. I mean, if you look at an interesting question you want to answer - where are the necessary insights supposed to come from? You'll need various ideas on how to approach the question and good intuition regarding what might work and what probably won't. Playing around with lots of interesting stuff whenever you have some time left is a very good way to get this kind of ideas and intuition. Oct 20, 2023 at 20:43
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One of the issues about being at a small college is that the local faculty in your field is also small with fewer opportunities for collaboration.

My main suggestion is that you find ways to increase your circle of contacts/collaborators by doing things like attending conferences and speaking to a lot of people about ideas. You can, perhaps, invite someone to your college to give a talk and spend a day or two in discussions. You can reciprocate by speaking to students (and then faculty) at other institutions. Anything that gets you in contact with people with whom you can share ideas.

At a large university a lot of this sort of thing happens in the coffee room, but you don't likely have that opportunity.

If you are in a metro area with other colleges and universities, find a way to visit, both at your institution and at theirs. If you are near an R1 (or similar) that has a research group in your subfield, try to get connected to it. Even another local SLAC will have faculty that might be interested in a working group.

Yes, it requires some funding. If your college in interested in your research development it can, perhaps, make those funds available. You can also look for grant funding for such things. In a few places it is even possible to obtain a bit of funding for travel and professional development from local industry.

Math, as you have learned, is very difficult to do on your own. The wider the circle you can build or get attached to, the more ideas that will float around, some of which that are worth pursuing.

Also, look to the previous contacts you had as a student and as a post-doc. Those people probably already have a circle and you might become a part of one or more of those.

Finally, share your own ideas. It is a good way to get feedback. Think in terms of joint authorship in the short-medium term.

I too was once very isolated, though in CS. Over time I built a very wide (international) group of collaborators. It took lots of travel, both in the US and internationally to build that circle. But we were, as a group, very productive. If you bring the people together, ideas are likely to flow.


One way that you can increase your value to your own college and make it more possible to get invited to speak at other colleges and universities is to develop a lecture or two on some topic of interest to you but that isn't part of the normal curriculum. You could do this at a level appropriate for either (or both) the graduate and undergraduate level. At the graduate level it might be based on your dissertation. At the undergraduate level it might be some arcane topic in your field that isn't commonly taught. Then find a way to make it known that you are willing (anxious) to visit other places and give the lecture.

The lecture could be part of a regular course or an evening convocation. But then use the time available at the visit to discuss ideas with other faculty there. Build that circle of common interest that can lead to sharing and developing ideas.

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  • Thank you for the answer, I think you make an excellent point. Two things: 1) I'm hesitant to ask people to come visit, or take up their resources visiting them, when historically I've not been able to pull my own weight. 2) I don't trust my ability to ask reasonable questions, or answer their questions. Are there things I could be doing to improve those skills? Oct 20, 2023 at 0:16
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    It is practice that improves all of that. People might be more willing to share than you think. But focus on people with common interests as much as possible. In the short term, conference meetings might serve you well.
    – Buffy
    Oct 20, 2023 at 0:22
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    you have to try even if you can't pull your weight. maybe the worst case does come to fruition and people are mad at you for wasting their time - you have to at least try. it might not turn out that way and a self-defeating attitude will only compound this issue. maybe they see that you're at least trying very hard and they're willing to mentor you in some sense. Oct 20, 2023 at 9:24
  • Thank you @giorginguyen, I needed to hear that Oct 20, 2023 at 13:03
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    I think that a professor's standing is enhanced if they get invitations to speak at other colleges and universities. I wouldn't treat it as a burden on them, but an opportunity for them.
    – Buffy
    Oct 20, 2023 at 13:09
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Math research is hard. If I'm not mistaken, about half of all authors in the Mathscinet database have exactly one paper, and those are mostly people who wrote a paper for their dissertation, moved on to a teaching-oriented position, and never published again.

One possibility you might want to consider is moving to an easier area of mathematics. You don't have the large chunks of time and energy needed to think deeply about deep abstract questions in algebraic topology? Do graph theory and work on graceful labellings of near-catepillars or something like that - still math research, but not requiring a ton of background or long stretches of dedicated time. Or do applied research that isn't really generating new knowledge but making somewhat routine applications of knowledge to questions no one has done before. (e.g. this has been done, so you'll have to find something else, but write a Monthly paper explaining the Markov chain for the runs expected table in baseball.) Or do scholarship of teaching and learning on how various methods work in your classes - this isn't mathematics research but it's still research. All of these activities keep your research mind active and have benefits for your students similar to that coming from traditional math research, so it's all good from your college's perspective.

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    @WolfgangBangerth Let us be honest: the difficulty of doing research varies wildly from area to area. There exist various "studies" where it is not easy to distinguish bona fide research from imitation -- as was recently highlighted in the famous Grievance Studies Affair Oct 20, 2023 at 4:04
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    @WolfgangBangerth Critical theories and other garbage aside, the difficulty of doing research varies considerably even over bona fide areas. Established in my area (which is at the overlap of astronomy, physics and applied math), I once attempted to get my foot in the door of pure math -- and had to acknowledge that it was too hard for me. One's success in applied math or astronomy doesn't serve as a warranty of success in pure math -- because pure math requires more talent and a stronger ability for abstract thinking. This is how it is. I learned it hard way: "math research is hard". Oct 20, 2023 at 4:23
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    @Michael_1812 Well yes, "math research is hard". But "physics is hard too", and "education studies are hard too". To claim otherwise would mean that the people in these areas are not also smart and driven and hard-working, and let me tell you: They are. Oct 20, 2023 at 14:22
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    @Tom: and Bott started in engineering. But these are statistical outliers, I do not think the OP is in that league. Oct 20, 2023 at 21:50
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    I don't think doing math well is inherently harder than other fields, but it's fair to say that publishing in pure math is hard. In all fields you need to come up with an interesting research topic and a sensible plan of attack, but math is one the fields with the fewest ways to publish inconclusive results. In applied fields, a rigorous experiment that fails to support your pet theory can still be published as useful evidence that'll guide the next plan of attack... but in math, it's hard to publish "I tried these approaches to this proof but none of them worked."
    – civilstat
    Oct 21, 2023 at 1:03
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My situation was similar to yours, but I had no active collaborations for several years and even was arguably outside of math during postdocs. I was TT at a SLAC too (now at a different institution that is basically a SLAC too but much better in every way, and tenured).

I essentially forgot about research for a few years, then decided to get back to it. I actually just started studying hard to relearn many things I forgot and to actually learn the things I never understood. It took a few years of intense study and research and then I finally got a small result. Kept working very hard, and now the results will not stop coming.

For me, it was a matter of very long hours dedicated to intense study in order to learn the things I wanted to understand. Couple that with teaching and administrative duties, and it is very intense.

I too feel like I am not good at math simply because I'm not as good as I'd like to be. That's ok. Somebody has to be in the middle or lower half in terms of overall capability/productivity. I probably would not survive at an R1. I would love to collaborate with others, but just haven't been able to connect with anyone. I feel like I still have to prove myself worthy of collaborating with. I hope the onslaught of papers I have in the works will do that finally. But if not, no big deal, I keep doing my thing.

It's hard to say how to come up with new ideas. I just work on things and questions just naturally arise, so I explore those, and sometimes they lead to something I feel excited enough about to write up. I cannot write unless I'm motivated about the problem. Most ideas end up nowhere or at a dead end with no insight on how to proceed. Recently, I solved a very hard problem (for me) that really required filling in many gaps in my knowledge and fixing many errors in my arguments. I was just lucky enough to manage to find enough drive to keep going.

I hope you find this helpful. My recommendation is to just work hard and study hard and try to think of questions to ask and how they might be explored.

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It sounds like your core problem is just coming up with ideas.

Is there any bright, motivated graduate student--or even an exceptional undergrad--who has good ideas, and could benefit from the resources, credibility and experience of collaborating with a PhD? Or maybe that just have intriguing concepts coming out of their thesis work that they don't have the time to explore themselves?

Obviously you would need to work hard to make sure it's an ethical, mutually beneficial relationship, not an exploitative one, but it's one possible avenue to explore.

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  • Thank you for answering. It's not just coming up with ideas, though that is part of it. It's also that, even once I have ideas, I don't seem to be good at solving the problems either. Oct 20, 2023 at 15:29
  • Well, that's the work of it, isn't it? Maybe with less experienced collaborators, you might be able to play a larger role in making forward progress. Oct 20, 2023 at 15:45
  • That is the work of it... That's the part that makes me feel like I'm a calculus student whose spending hours diligently highlighting their textbook; I feel like I'm doing the work in the wrong way, but I don't know how it's wrong. Oct 20, 2023 at 19:47
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If everyone in academia's main strength was coming up with good research ideas, academia as we know it would cease to function (some might argue that this has already happened, but that's for a different post). Every research grant is basically it's own tiny company. Somebody has to manage finances, identify and recruit talent, manage projects, communicate results... the list goes on (see CRediT authorship statements for a starting point). Finding people who can do those practical things AND understand the deeply technical stuff is enormously difficult. Let's assume that you know yourself and that you're bad at generating new research ideas. So what? Identify the parts of research that you ARE good at. Once you've done that, follow Buffy's advice and network your butt off to find other researchers whose strengths complement yours.

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    What you describe is quite typical for lab sciences but this is not how it works in math. Oct 20, 2023 at 16:40
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A few suggestions:

  1. You've mentioned that you have ideas for research problems to tackle, but not for how to approach them. Can you make a list of the problem-solving techniques you've used successfully in the past? I think it was Feynman again who recommended keeping a mental list of about a dozen problems to solve and a dozen problem-solving techniques. Every time you go to a talk or read a paper, see if their problem can be solved with one of your techniques, and whether their own solution-technique could work for one of your problems.

  2. Related: Go talk to people in other fields who use pure math: for instance, statistical methodology or theoretical physics. Describe the kinds of problems & techniques you are familiar with, and see if that spurs ideas they could use in a collaboration.
    I am not suggesting that you switch to applied problems and analyzing data yourself -- that takes its own specialized expertise! Rather, maybe you have a research focus in abstract algebra that turns out to be incredibly useful to a mathematical statistician who's gotten stuck on a problem in the theory of experimental design, for example.

  3. Can you combine several disparate interests? Perhaps you are not solely an expert in just one very narrow topic, but rather you are pretty competent in several topics?
    (Personally, I have some experience in two distinct subfields of statistics that haven't traditionally overlapped much. I'm not one of the leading experts in either topic alone, but I'm carving out a niche as one of relatively few people who have the experience to sensibly combine the two.)

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The best advice I ever heard on the matter came from the chair of a small liberal arts college I used to work at. He advised that people should not get stuck working on their thesis indefinitely!

He believed that despite having a Ph.D. in an X field, there is a lot to be gained by switching focus to working on projects related to a Y field, even if Y might be completely unrelated to X. I started having some research results once I started doing that, however, there is still a lot of work to be done.

About finding research groups to work with, I think it's good to work on something small related to their research and once you have done something, ask them for help/guidance.

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