Tenure Track at a Small Liberal Arts College, but bad at research, how do I improve?

Question

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.

Answer 1

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.

Answer 2

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.

Answer 3

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.

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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.

Answer 4

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.

Answer 5

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.

Answer 6

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.

Answer 7

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.)

Answer 8

I'm a math professor at a small liberal arts college (SLAC) and now I have junior faculty who I mentor. Until you have tenure, the advice is to find a way to do sufficient research to get tenure. Here are some ideas:

• Depending on the SLAC, it might or might not be a problem to co-author things with your advisor. If you need one more publication to get tenure, your advisor might be happy to loop you in on something, e.g., with the current PhD students, that could result in a publication for you (provided you do your part of course) and valuable mentorship for your academic siblings.
• It's unlikely that a SLAC would insist you write solo-authored papers, so collaborators could help a lot. I echo the advice to make contacts at nearby universities (I did that, co-authored papers with OSU professors, and regularly attend the OSU seminar), and invite speakers whose research interests you. If you have broad interests, consider inviting someone who seems to be looking for co-authors, e.g., someone working to develop a course in social justice math (if that's something you're interested in), someone working on math to identify gerrymandering, etc.
• Does research with undergrads count? At many SLACs, it would. I supervised undergraduate research many times. It's more like teaching. The student takes an upper-level elective with me, does a final project in the course, then builds on it during a directed study the next semester, culminating in some new results publishable in an undergraduate journal. If you need the publication, you can probably be a co-author on that paper (I published such a paper, not because I needed the publication, but because that specific undergrad journal required a faculty co-author, and I'd done a fair bit of work on the paepr). For some SLACs that might look even better than a solo-authored paper in a professional (not undergrad) journal.
• Does scholarship of teaching and learning count? If you've been teaching at a SLAC for several years, odds are you've created a new course. You could write up an article for PRIMUS or another such journal, about the course, why it's valuable, how you developed it, what materials you developed (e.g., real-world applications, projects), and what the students thought of it (from their evaluations). I published a paper like that.
• Does the scholarship have to be in math journals? If not, you could join forces with someone in another department, to help them with their work. Often, the level of math this requires is very low, e.g., just a bit of algebra in order to create game theory models (I published a paper like that) or a bit of R programming to run a simulation (I'm working on such a paper right now). I'm very driven by wanting to be a loyal friend, so even if I am personally not that motivated to work on something, I'll do it if a friend wants me to. I've also done a few papers that amount to statistical consulting (my training is in topology, but I teach stats), for similar reasons.

After tenure, you can re-assess what gets you excited, and adjust your scholarship in that direction. Plenty of SLAC professors shift into writing textbooks, scholarship of learning, etc. But the essential thing right now is to get tenure, even if it means doing work you are not that excited about, knowing that you having tenure is what's best for your department, university, and students, and post-tenure you can readjust.

Answer 9

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.

Answer 10

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.