Lets say you had an undergraduate who wanted to do some advanced work and some research, possibly for a thesis, or things like that.

There are two slightly more specific groups of questions I have about this process:

  • How would you go about choosing a problem? Specifically, should the student work on open problems or work through existing proofs? Are there lists of problems at that might be fruitful and approachable?
  • What sort of guidance would you provide them? With what frequency would you meet? Would your meetings be closer to teaching or guiding them along on their own?
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    $\begingroup$ I think this question is pretty broad. -- Could you maybe narrow it down a bit? $\endgroup$
    – Stefan Kohl
    Commented Apr 6, 2016 at 20:22
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    $\begingroup$ That was kind of intentional, but at the same time I can see that making it hard to answer- I'll try. $\endgroup$ Commented Apr 6, 2016 at 20:24
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    $\begingroup$ There are very successful advisors at both ends of the spectrum for the second question, and a similar thing is probably true for the first question. I'd imagine this depends hugely on the student, and perhaps how much background the student needs to know to do research on a specific problem. I'm sure some of the very smart and successful people on this site have some insight and opinions a lot of people will agree with, yet I still feel this is close to purely opinion based. $\endgroup$
    – PVAL
    Commented Apr 6, 2016 at 20:44
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    $\begingroup$ For the second block of questions — this definitely depends more on a specific student rather than on whether he is a graduate or not. Some people need advising, some prefer to work on their own. The goal is to become someone who can mostly work without other's help, but you don't just magically transform into one the moment you graduate. $\endgroup$ Commented Apr 6, 2016 at 20:55
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    $\begingroup$ discussion in and below this answer (math.stackexchange.com/questions/1730964/…) can be an interesting problem to work on. At least the problem itself is very easy to understand. $\endgroup$
    – user288447
    Commented Apr 7, 2016 at 1:25

5 Answers 5


As a former faculty member in several elite college and university departments, I have worked with and mentored a number of talented undergraduate and graduate students including several mathematics students. The advice I give to a student in this regard depends on the student's interest, and greatly upon the student's career goals. Students who pursue mathematics as a tool and firm background for a career in other technical disciplines (e.g., computer science, physics, electrical engineering), are most likely to profit from working on existing problems, even deep ones whose roots lie in other disciplines. That's what their career will likely entail.

If however the student seeks a career as a professional mathematician--particularly an academic, research or "pure" mathematician--the student must become expert in identifying and creating new problems. For such students, I would counsel they immerse themselves in their favorite subdiscipline and spend some time creating the problem, or modifying a recognized one.

Being able to ask the right questions and identify new problems is a talent that distinguishes the greatest mathematicians (and scientists) and is, alas, rarely taught or even encouraged in most academic departments. I published a peer-reviewed research paper with an extremely talented undergraduate mathematics student who solved a problem that I posed. (I was not his senior thesis mentor, however.) When he went off to one of the leading graduate mathematics departments he found that he could not identify new problems. Last I heard he dropped out of graduate school and programmed computers for a traditional bank.

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    $\begingroup$ +1 for the second paragraph- that's uncommon advice, but I love it $\endgroup$ Commented Apr 7, 2016 at 1:26

I have only advised a few undergraduates on projects like this, although I participated in several undergraduate research projects including an REU and a baccalaureate thesis.

The choice between working on open problems versus reading existing proofs is a false dichotomy.

First, it is common to have students do both: Have them read through papers you select and work on a problem.

Second, those aren't the only two options. There are many things that are not known that are not called open problems. A student can collect data testing a conjecture, and this can range in difficulty from a straightforward calculation or programming exercise to something requiring real ingenuity to check examples with intrinsic interest. A student can apply a result to a case of interest.

There are many questions mathematicians ask that are not universally called open problems because people haven't looked at them much. This happens at the ends of many papers and many talks. The author of a paper might be saying, "I think the techniques used in this paper will work on the following problems but I don't have time to look at them." These are often much better problems for students to work on than problems that are known to be open because many people have verified that the easy/standard techniques don't work.

Part of mathematics is exposition. You can ask a student to rewrite a known result using better notation or filling in the details. When a result was a culmination of multiple papers, it might be that the overall exposition is very different from what it should be. Fixing that might be a good task for a student... or it could be far too hard, and a good task for a team of seasoned mathematicians, as in the case of the classification of finite simple groups. Many masters theses are improved expositions of known results. I have found a lot of nice expositions written as senior theses.

Advising undergraduates properly can require a significant amount of preparation, and it should not be undertaken lightly. I think you should focus on the educational benefit to the students instead of the potential value of the research, so lean toward having the undergraduate read good papers and pick up useful ideas and skills over having the best chance to produce research. Further, the student is likely to run into obstacles and may be unable to produce new research within the short amount of time allowed. When that happens, will the student have something to write up anyway? Try to make a project with many ways to conclude well such as expositions and partial results. It is easier (but not necessarily easy) to schedule progress through experimental calculations, reading, and expositions than it is to plan on research progress.

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    $\begingroup$ I think this is excellent advice. Particularly there is always great need for excellent exposition, and I have found that the Harvard senior theses math.harvard.edu/theses (where, as I understand it, the student is expected not to solve an open problem) are admirable examples and undoubtedly provide great training. (I also regard thoughtful exposition -- effective arrangement of the facts -- as a creative act of research.) $\endgroup$
    – Todd Trimble
    Commented Apr 7, 2016 at 11:57
  • "...should the student work on open problems...?"

I think that working on open problems is fine—even exciting—if you follow Pólya's advice in How to Solve It:

"If you can't solve a problem, then there is an easier problem you can solve: Find it."

Just as one example, it is unknown whether or not it is decidable if a given single polygonal tile can tile the plane. It is unknown even if the tile is a polyomino. I supervised a very nice undergraduate exploration of this question for specific polyominoes.

If you simplify the question enough, you can solve it. Then generalize until you cannot solve it. And so on, oscillating above and below.

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    $\begingroup$ I have seen the quote given as, "If you can't solve a problem, then there is an easier problem you can't solve – find it!" E.g., page ix of Murty and Esmonde, Problems in Algebraic Number Theory. $\endgroup$ Commented Apr 6, 2016 at 22:57
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    $\begingroup$ @GerryMyerson: The quote is on p.114. Both make sense, and make the same point, but I believe he phrased it in the positive rather than the negative. $\endgroup$ Commented Apr 6, 2016 at 23:09
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    $\begingroup$ @GerryMyerson: I took your remark to be questioning whether I quoted correctly. Concerning the can't-can't version, it makes kinda ironic sense (to me). $\endgroup$ Commented Apr 6, 2016 at 23:21
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    $\begingroup$ @GerryMyerson: By induction the statement in the quote leads to a contradiction. It reminds the Sorites paradox also! $\endgroup$
    – user288447
    Commented Apr 7, 2016 at 1:34
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    $\begingroup$ @Edi I think I can produce an infinite sequence of successively weaker statements, none of which I can solve. $\endgroup$
    – Kimball
    Commented Apr 8, 2016 at 2:44

To give a viewpoint from the other side, I am an undergraduate B.S. student in Engineering, and spent the last year on a research in the Biomedical Engineering area, in Brazil.

It was based on a hot-topic of the area, and my part on the research was to verify the usability of a method invented by my mentor. So, to answer your first question, working on open-problems is very interesting to a student, as it gives you the opportunity to do something no one has ever done before, even if it gives no relevant results.

As it was a research in which I could do most work at home (programming, reading articles, etc.), my mentor and I would encounter only once a week. Each week my mentor would give me some guidance as "what to do this week", and see what I have done in the past week. We would also discuss through e-mail, when necessary. This would make sure that I was progressing in the research, and if I was not, we would discuss what should we do as an alternative.

So, answering your second question with my own experience, it was very important a regular meeting, with a goal between two of them, so that it would progress on a regular basis. More than once in a week probably would result in many goals not achieved, (which is demotivating) and less than once a week would be a very slow-paced research, with less guidance (also demotivating). So once a week worked really fine for us.

Also, you should always ask the student what he thinks could be done to solve the next step of the problem. If you don't agree with him, try to make him explain why it is a good idea. If you're still not convinced, say to them why you think that won't work, and maybe give another way to proceed the research (stating things like "I strongly suggest you do this next, instead, because of (...)"), but let him choose what should be done next, as it's his research.

Also, leave all the learning to the student. He is learning how to make research, not how to do something. You could recommend some textbooks and/or papers to read of the related theme, but it is not your job to tell him what the books/papers states. Also, it is a good idea to ask the student to give an presentation of what the papers are stating, on some of the meetings. This way, he would also be learning how to learn, instead of just learning a tool to make progress with his research. This will be very important when he starts his Master's.

This was how I was mentored. This made the research both interesting and fulfilling to me, as an scholar, and resulted in a published paper on the biggest international conference in Biomedical Engineering.

Just to be clear, again, I'm only stating my own experience as a mentored undergraduate student, that worked well for both me and my mentor. I hope that helps!


I offer this answer with a disclaimer. I am an entering graduate student and have no experience mentoring undergraduate research, although I did do some undergrad research.

I can't tell you what to research, or how often to meet, or how to specifically guide, but I can tell you, what is in my opinion, the right mindset. Very few undergraduate research projects result in important results (I'd be curious to see an example of one though!). The point of undergraduate research, in my opinion, is training. It is to teach a young mathematician the tools they will need to succeed in whatever path they are currently intending; industry, research in pure or applied math, etc.

I'll explain my undergrad research, which if I could be frank is not research in the sense that I solved an open problem; my senior thesis was entirely expository. I investigated the relationship between Brownian motion and PDEs like the heat and Schroedinger equations.

During my investigations, my adviser taught me a lot of various areas. I learned PDEs, probability, stochastic processes, Fourier analysis, functional analysis, quantum mechanics, statistical mechanics, etc. Sometimes he would just teach me things unrelated to the project, just because I asked a question and/or he thought it was important.

What I think is important is learning the tools of the trade, whatever the student needs to succeed in their intended career path. I was introduced to a really interesting and exciting topic, which was bonus. Currently I am intending on researching SPDEs and rough path theory. This may change, but no matter what, as a researcher in math I need to know functional analysis, etc. if nothing more than to pass my quals (studying for these have been considerably easier because of my project).

tl;dr The topic itself matters less than the tools you teach. It is more important to teach the necessary tools to succeed in research than to actually produce real results.


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