How exactly do Math theses/dissertations work?

Is it fair to assume that the work involves trying to prove something? What happens if you can't?

I did a thesis in Computer Science, and though my results weren't great, I still had something to show. I learned from it and had a plan for future work.

But if you have X years to prove something for, say, a PhD and you can't, what happens? Do you just not get a PhD?

I understand that advisors will try to pick a problem that they think is doable, but what if they misjudge?

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    I often heard the phrase "If you can't prove it, prove something else." It's often possible to salvage the work by relaxing the conditions of the statement you wanted to prove.
    – Turion
    May 12, 2016 at 11:40
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    "Relaxing the conditions" gives you a better result too :) May 12, 2016 at 18:56
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    This happened to every math PhD student I knew.
    – user37208
    May 13, 2016 at 1:54
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    @darijgrinberg It also makes the conditions feel less stressed ;)
    – Michael
    May 13, 2016 at 16:46
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    @corsiKa: Who says that the breakthroughs would guarantee their authors funding? :) May 13, 2016 at 17:00

7 Answers 7


I wrote a failed dissertation myself. No papers resulted from it. Fortunately, I had a significant side project which was published, and 11 years later, the main thread of my research still comes from this side project. (I suppose I could have written up the side project as my dissertation instead, but I didn't.)

First, no project is ever a complete failure. At the very least, you manage to prove some (possibly almost trivial) special cases, you prove some helpful lemmas, you find that certain lemmas you might have hoped would be helpful have counterexamples, and you find certain methods that you might use don't apply because some hypotheses needed to use those methods aren't satisfied in your case. It's possible to write all of these things up, ending up with a dissertation that's basically about "How not to solve Problem X (except in this very tiny special case)". (This is basically my dissertation.)

Second, it's rare for mathematics graduate students, especially at top programs, to work on only one problem. Your advisor might suggest a main problem for you to work on, but you go to seminars and hear about other problems, talk to other graduate students or postdocs and learn about other problems, and so on, and graduate students are generally encouraged to spend at least a little time thinking about these other problems. If you get stuck on your main problem, you still have other problems to solve, and it's quite common that what you learned to work on your main problem ends up helping you in solving these other problems instead. (This is basically what happened to me, except this other problem didn't end up in my dissertation.)

Third, especially in the early stages of working on a problem, advisors are usually fairly quick at pulling the hook if it looks like no progress is being made. Most advisors know of lots of problems, and they know what complete lack of progress due to a problem being too hard looks like. Even later on, advisors can sometimes suggest simpler problems that can be solved in a shorter time frame (given what a student has already learned). In some cases, after a few rounds of failed problems, the student ends up with a dissertation that's about as weighty as a half-decent undergraduate research project (and results in zero papers or one paper in a "write-only" journal).

It's true that a dissertation written out of a failed or almost trivial project tends not to bode well in applications for jobs where research matters (unless there is a more substantial side project). Sometimes an influential or convincing advisor can make a strong enough case in recommendation letters for the student to get a postdoc, but this is harder now then it was 10 years ago given how much more competitive the job market is.

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    Out of curiosity, did your exam committee have serious problem with your dissertation?
    – Nobody
    May 12, 2016 at 5:12
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    @scaaahu: IIRC, I cleared my approach with my committee before doing much of the actual dissertation writing. They could have asked me to write instead on my more successful projects, but they didn't. May 13, 2016 at 10:48
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    Comments are not for extended discussion; this conversation (which was very interesting - so please do follow the chat link if you want to read more) has been moved to chat.
    – ff524
    May 16, 2016 at 9:39
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    +1 for "First, no project is ever a complete failure." This is something that should be taught more often in academia.
    – jwir3
    May 16, 2016 at 14:56

A good advisor will steer students away from "all or nothing" problems, the sort of problems where complete failure is a realistic possibility. For example, one stereotypical case is an elementary attempt to resolve a famous question in number theory, where the most likely outcome is a concrete understanding of why this specific approach just can't work, and nobody else will be terribly interested since they never thought it had a chance in the first place.

A good thesis problem needs to have several properties:

  1. It should be interesting and attention-getting if solved. This is the easy property to achieve.

  2. It should be in a rich and diverse enough area that any serious attempt to solve it will uncover something worthwhile in its own right, even if it doesn't lead to a solution of the original problem.

  3. It should help the student build knowledge and prepare to branch off in several new directions. (I.e., you shouldn't reach the state of being done with nothing more to do, and continuing work should naturally grow broader rather than narrower.)

In particular, #1 is far from enough by itself. If you have #2 as well, then it doesn't really matter whether the original problem is solved, while #3 is important for setting the student up for success beyond graduate school.

So the optimistic answer to your question is that the advisor should take care to prevent this from becoming a problem, by guiding the student to a problem where failure to solve it is not a disaster. Of course there's also the pessimistic scenario in which the advisor screwed up or the student wouldn't take advice, and the problem really isn't suitable for a thesis. In that case you have to muddle through as best you can, probably by writing a suboptimal thesis and then trying to make up for it by other work afterwards. Fortunately this scenario doesn't seem to occur all that often. (And the worst case of all is when the student just isn't accomplishing anything, but that can happen in any field.)


There are a number of successful outcomes that don't involve finding that desired proof. Here are some examples:

  1. Very often, a good mathematical question is good not simply because the answer would be useful, but because the techniques that might lead to an answer are useful. If you develop new mathematical tools, those might form a worthy thesis in themselves even if they don't amount to a proof.
  2. You may achieve some intermediate result that opens a new possibility to prove the bigger result. Indeed, many theses only aim for this if the bigger result is something huge like the Riemann hypothesis, the BSD conjecture, etc.
  3. In searching for a proof of X, you may discover a related question Y and find a proof that resolves Y. Y might be more interesting than X, or simply more approachable. This is discussed in Uri Alon's well-known short paper on choosing a problem; I recommend that paper to anyone who is asking this question.

A good advisor will help you find a thesis topic that has multiple avenues and multiple stages of potential progress, so that it is not an all-or-nothing venture.


My stats professor last semester said that she is saddened by the fact that journals no longer tend to publish failed studies/theories. A failed theory is just that, it shows you had a theory, but you proved it wrong! That is an incredible amount of information and if you combine that with multiple other studies that show the same thing, you have mounting evidence that the theory is wrong. For instance, if we only publish the successful theories/studies, we are biasing our results in a sense, because there may have been 50 studies that show there was no evidence for the theory being true, but if there was one single study, who just barely made it over the threshold for proving the theory true, that one could have been published and now boom, the only published information about said theory is one that "proves it true". I am also not a math major, but I thought this was an interesting topic enough to share with you. The result of an inconclusive experiment still holds a very large amount of data that could still be very important to someone else years down the road.

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    With regards to stats, I think that's a slightly different angle. I believe your professor was speaking in regards to scientific questions that require empirical evidence: "does coffee increase risk for heart attack?"; you can't prove that logically, but you can collect a lot of data and make a conclusion. As such, I agree that a paper stating "we observed 100,000 patients and found no connection between coffee and heart attacks" is worth publishing, yet I would be a little more hesitant with a paper that states "I tried to square the circle for 10,000 hours and was not successful".
    – Cliff AB
    May 13, 2016 at 4:26
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    @CliffAB: in fact the growing trend to demand pre-registration of drug trials is on the basis that if you observe 100k patients and find no connection between coffee and heart attacks then it's unethical not to publish that fact simply because it's not the result you hoped for. May 13, 2016 at 11:34
  • That is very good to hear. and yea, @CliffAB i definitely agree with that, we don't need inconclusive results from a theory/thesis that has no reason to even be tested.
    – Adam Pine
    May 13, 2016 at 21:19
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    @CliffAB: and in addition papers differ from theses in that the paper should concentrate on the increase in scientific knowledge, whereas a degree should be awarded on showing that the student mastered their required professional working techniques. The scientific advance then is a surrogate marker for the "worthiness of the degree" that works for positive results, but doesn't say much in case of negative results as they can be due to the object of the work being truly impossible (or not attainable with a reasonable level of professional ability for the degree in question). May 14, 2016 at 9:48

Is it fair to assume that the work involves trying to prove something? What happens if you can't?

No. Not all theses are about "proving things," at least not in the narrow sense. A thesis may be very computational, may be about formulating conjectures, or it may be about finding examples/counterexamples of some phenomena. Many theses (and papers), even if they prove a theorem, boil down to understanding some theory and doing some (not necessarily numerical) calculations.

As Alexander Woo says, even if you can't prove what you set out to, you can typically find something new (sometimes just a new point of view) if you're reasonably competent and spend enough time on it. Actually it's more common than not, even for professional researchers, that you don't prove what you set out to. I didn't prove what I tried to for my thesis, but I got some results and a couple papers out of it. Several years is plenty of time for most people to get at least something.

But if you have X years to prove something for, say, a PhD and you can't, what happens? Do you just not get a PhD?

As I said, the chance is good that you will at least get something new, or you may move to another project when it seems hopeless. Your advisor will hopefully help guide you and keep you from following dead ends for too long. I try to make the projects for my students in areas where there are lots of nearby problems, so if their project doesn't work out, they don't need to learn much more to try a different problem. When your advisor thinks you have enough for a PhD then you can submit a thesis, but of course you don't get a PhD just for having worked on something for X years.

I don't have hard data on this, but my experience is that most PhD students who make it through the first couple of years (say, at good schools in the US) do get a PhD. Where I went, almost everybody who started got a PhD--and almost all of the ones who didn't left during or after the first year because they realized a PhD wasn't for them. At less prestigious schools, the success rates aren't quite as good, but I still think most of the people who don't finish their PhD quit before they spend a long time on research.


One case:

I had in mind an interesting problem. I thought of the absolute simplest case, and gave it to the student to work on. After that I thought we could try more general cases, working up gradually to the whole thing. Well, it turned out that initial special case took two years for the student to finish, so that was the thesis. (As far as I know, the more general problem has never been done to this day.)


You're not always trying to prove an existing theorem. In my experience, the central theorem(s) of the thesis are not known initially. You tackle a rough problem and try to find some new results - in my particular case, it was about analysing a situation where partial results existed, but no reasonable estimates for some of the constants had been found. My central result was a theorem characterising situations where you could find optimal constants, plus how to actually compute them.

I had the same problem with 'no results' initially though - in the end I had to select a new topic after 2 years. There were still some results along the way, though. Even if the main proof won't work it's unlikely you won't even get some partial results or discover something new along the way.

I was still able to fill about 30 pages in my thesis with the results I had from the first topic. It wouldn't have been enough for a PhD on its own, but it wasn't nothing either. It helped that the topics were similar and one could draw a few parallels.

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