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I am a graduate student in Mathematics. I have solved my original thesis problem, and that will probably one or two papers, at least one of them very good. After that, my advisor basically told me: "Here is this paper that I wrote (together with two other very strong professors), there are some cases missing, I would like you to do them". Problem is, none of them has an idea on how to solve these cases (otherwise they would have written them in their paper, of course), so here I am, stuck on this problem for months, with basically no advance whatsoever (at the beginning at least I was learning a lot of stuff, now I know everything that's relevant that's been written up to know - I spent a lot of time looking at the literature). How can a PhD student (decently good, but certainly not a star) be expected to improve upon the work of some professors, if there nobody has a precise idea on how to do so? I think this is overambitious and nonsensical, to say the least (especially after spending 3-4 months on it).

It is one of those problems where once you have found the key idea, the problem is completely done (exactly the opposite of what I like working on).

I would like to work on other lower risk projects, but my advisor made it pretty clear that he wants me to spend time on this, so I would be completely on my own. I don't think I can come up with something new just on my own, but I think that spending other months trying to outdo professors is not going to work either! What should I do?

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    "Problem is, none of them has an idea on how to solve these cases (otherwise they would have written them in their paper, of course), so here I am, stuck on this problem for months, with basically no advance whatsoever". This doesn't make it a nonsensical project -- at most an unfitting one, but even this is not necessarily clear after a just a few months. Mathematicians often have some feeling about what problems are likely to be hard and what ones aren't... and half of the time that intuition ends up being wrong. – darij grinberg Apr 4 '18 at 22:09
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    Ask around, don't just read -- some ideas may be floating in the community, never written up. Move laterally: try solving similar questions that haven't been asked yet (these will probably give you less fame per problem solved, but should be easier). Few PhD theses end up solving the exact question that was asked. Many are lateral (they ask new questions and only solve those). Many classical results of abstract algebra came out of people's trying to prove Fermat's Last Theorem. – darij grinberg Apr 4 '18 at 22:11
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    Related: What's a good way out when research is stuck? – user37208 Apr 4 '18 at 22:14
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    As a first approximation, you will not be able to get a tenure-track job at a research university without solving at least one problem that no one has any precise idea of how to tackle. You might as well start trying now. – Alexander Woo Apr 5 '18 at 2:20
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I think you should stick with it.

As far as my understanding goes, publishing 1-2 papers as a mathematics PhD student is (more than) enough to get your degree. It may not rank you as a star but it's a solid proof of competence. Working on other lower risk projects may not improve your thesis significantly. Successfully completing a high risk project, however, will be a boon to your PhD.

Furthermore, this project yanks you out of your comfort zone where you can gradually work towards a solution. Instead, you now have to find one key idea and you're basically done. Again, you've already shown you're a good mathematician inside your comfort zone, so showing that you can solve those kind of problems should not be your main priority.

I think your advisor has a high opinion of you and wants to give you an opportunity to prove exactly how much you're capable of. That's a nice vote of confidence. If you actually do want to stick with it, it's probably a good idea to find ways to enjoy the project. Possible ideas: talk to other people about the project, especially to your advisor and the other two professors. Sometimes spend as much time as possible trying to find a solution even if you feel it may not work. And sometimes work on unrelated fields or do other stuff (such as teaching) that is both inspiring and relaxing.

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Not being in a mathematics field, my experiences may not be absolutely translatable but I think in general the issue is pretty much the same. You work on a project for x amount of time with y output. If x starts getting too big with a small y, then you start not wanting to spend any more time on it and wish to pursue other projects, related or not to the original problem.

It is not enough to just say to your professor, however, that 'I have spent x amount of time with a tiny y, therefore I do not want to do this anymore'. You need to justify to them why the project is a) unviable and b) an alternative means to answer the same question or justification to work on something else. If you simply say you don't want to do it because it's too hard, I daresay they'll tell you 'tough-luck, stick with it'.

A PhD is meant to challenge you and push your level of expertise beyond the current abilities you hold, and this might mean struggling for 6 months to a year (or beyond that!) on a project. I would hazard a guess that your professor is aware of your capabilities, seeing as they wanted you to do a PhD with them, but instead of simply saying 'I am incapable of completing this' perhaps ask yourself or your professor 'What do I need to do to become competent enough to complete this?'

If this project does not absorb 100% of your time, I would suggest finding side projects that you can manage when things in the original project aren't working or you're burnt out with it.

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When you start a PhD, typically you need a lot of help to find something suitable to study, and your supervisor knows a lot more than you about the subject.

By the end of your maths PhD, the situation should be different: you should be coming up with your own projects, about which you know more than your supervisor.

So while it is true that projects in maths can take a (very) long time, and that is no reason to give up, I believe you should also start to branch out on your own. Learning how to come up with projects yourself is part of the intended learning outcomes of a PhD, so even if you get nowhere it is not wasted time. Having more than one project running at a time has the advantage that when you get fed up with one, you can work on another.

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Solving unsolved problems is basically what PhDs are all about. The real question is whether this particular unsolved problem is germane to your thesis.

If it is, you either persist in solving it or you look for a different topic.

However, you say that you've solved your original thesis problem and have a couple of papers up your sleeve. If that means you have enough to write up and submit, consider treating the new problem as a side issue. Don't neglect the completion of your own PhD. It sounds unprofessional for an advisor to block progress on your PhD until you've solved an unrelated problem, but if that is case, consider having a chat with your university's administration.

The middle ground is that the new problem is interesting and important to your advisor, and that although he isn't blocking progress on your PhD, the new problem is taking time away from your thesis. In this case, recognise that your main 'job' is the thesis, and the new problem is an additional collaborative task . As a PhD candidate, you are considered something of a peer generally, and an emerging expert in your own area, so don't downplay your own abilities.

Treat this like a consultation (them consulting you). If you give it a good try and can't work it out, let them know. The primary authors aren't likely to just sit around twiddling their thumbs until you hit upon the solution because it's their paper, after all. So it's up to you whether you want to keep working at a chance to add your name to their paper, or to let it go because you need to complete your thesis (and your own two papers). Both are valid options.

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