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Okay. My questions are: How do some people do doctorates in mathematics and spend so much time like three to six years trying to answer one or two open problems? How do they have the patience, psychological strength, perseverance to solve those problems for so much time?

Other questions: People like Perelman, Wiles who spend seven years each one of them for the Poincare conjecture, Fermat's last theorem to prove them respectively, how do they do it? Do they know beforehand some of the possible ways to solve those problems? What should someone study to ultimately solve problems like those? How will he know if he follows the correct paths to prove them?

Should i try to solve problems that do not take so many years or months to solve at the beginning at least? Perhaps they take like two weeks or a month to solve or less than that? How could i find those open problems?

I am an undergraduate student in math at university. I try to read some math and physics that are not included in the material covered in my undergraduate studies.

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    $\begingroup$ Look up survival bias. You focus on examples of people who solved a famous problem without accounting for the many who tried and did not solve it. Consider also the role of being around at the right time. In the case of FLT, if Frey never observed that a counterexample to FLT should lead to a non-modular elliptic curve over $\mathbf Q$ then the path to FLT Wiles pursued would never have started. He would not have put aside everything for 7 years to try to prove modularity of elliptic curves over $\mathbf Q$ without having the motivation that it implies FLT (by the work of Serre and Ribet). $\endgroup$
    – KCd
    Commented Jan 1, 2022 at 15:54
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    $\begingroup$ Your question seems to be based on a misconception. Doing a PhD in math is, in most cases, not about "trying to answer one or two open problems". It is about diving into a particular (sub-)field of mathematics, understanding, exploring and developing (old and new) ideas. A specific open problem can sometimes be a useful guide to this end, but in many cases, the outcome of a PhD is a collection of various results and theorems in a particular field rather than the very solution to a specific single open problem. $\endgroup$
    – Jochen Glueck
    Commented Jan 1, 2022 at 17:17
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    $\begingroup$ If you'd like to try math research as an undergraduate, look into REUs (research experiences for undergraduates) or ask your math professors to see if they'd be willing (or know someone who'd be willing) to supervise a research project. $\endgroup$
    – TomKern
    Commented Jan 1, 2022 at 22:13
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    $\begingroup$ Just look up “survivor bias”. Maybe I should have called it “selection bias”. What I meant was focusing (in your examples) on results that were the highlight of someone’s career as if they just jumped right to working on that at some random time, when the broader truth is that lots of people had worked steadily on such problems and did not come up with a solution, and people don’t make a habit of reporting their failures (you singled out the two who “survived” to the end of solving very famous problems). What is more typical is to make just partial progress, and this is valuable too. $\endgroup$
    – KCd
    Commented Jan 2, 2022 at 16:14
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    $\begingroup$ In fact the solution to FLT depended on such partial progress: Frey’s offering was a new perspective on FLT, and he published it in the hope that others could build on it. Then Serre was motivated to make a further conjecture, Ribet proved Serre’s idea could work (that is, modularity of elliptic curves over $\mathbf Q$ really did imply FLT), and then Wiles proved enough of modularity to reach a solution of FLT. So the work of Wiles was itself a case of partial progress (on modularity, not FLT), and others built on his work over the next several years to fully settle modularity. $\endgroup$
    – KCd
    Commented Jan 2, 2022 at 16:24

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There is one trick that often helps even if you are not Perelman or Wiles: try to solve several unrelated problems simultaneously rotating the amounts of time you spend on each of them so when you feel that you are completely stuck on one, you concentrate heavily on some other one and think of the first one in the background until you get some fresh idea about it that you think is worth trying in serious.

In addition to reducing the frustration, this approach often rewards you with revealing some unexpected connections when the techniques that you try on problem X without success suddenly turn out to be applicable to problem Y while you would never think of using them if you concentrated on Y alone. I usually make my living as a mathematician from spending about 50% of my time thinking (with various degrees of success) on random questions that come my way from my friends, colleagues, or just complete strangers on MathOverflow. True, that strategy may be 50% suboptimal if your goal is to prove the Riemann hypothesis and you care about nothing else, but if you just want to have fun and establish plenty of contacts in the process, it pays off handsomely.

As to the dissertation, in my case it just came naturally from several topics I was thinking of even as an undergraduate. I just hid the failures (which constituted the overwhelming majority) and brought a few remaining successes to the light. That turned out to be sufficient. I should also say that I was lucky with my adviser who had an amazing skill of finding a problem matching the graduate student abilities and inclinations without having any idea of how to approach that problem himself. How that could be done still remains a complete mystery to me.

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At least at first (i.e. before completing your Ph.D.) it helps to have an advisor. She can "advise" you on this: When to stop working on that problem and try another; how to try first a simpler case; references to use to avoid repeating what others have done.

One of my fellow graduate students (1970s) wanted to solve the four color problem. His advisor said "no". Wait until after you have tenure to attempt that. If you really want to do graph theory, let's find a more reasonable problem for you to work on.

A story says someone once asked Hilbert why he never worked on the Riemann hypothesis. He replied that he would probably have to spend 5 years getting the background before he could attempt it, and he did not want to waste 5 years on a probable failure. [From memory, maybe the details are wrong?]

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  • $\begingroup$ In the versions of the quote I've seen, Hilbert's remark is in reference to Fermat's Last Theorem. These versions also say three years, not five. $\endgroup$
    – Will Orrick
    Commented Jul 9, 2022 at 3:11
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    $\begingroup$ Hilbert did, of course, have a great deal of interest in the Riemann Hypothesis--it was on his famous list of problems--and, although analytic number theory (according to Wikipedia) was not one of his areas of expertise, there's even an approach to the problem with his name on it, the Hilbert–Pólya conjecture. Another famous quote of Hilbert's: "If I were to awaken after having slept for a thousand years, my first question would be: Has the Riemann hypothesis been proved?" $\endgroup$
    – Will Orrick
    Commented Jul 9, 2022 at 3:11
  • $\begingroup$ In hindsight, I think maybe that anecdote was actually about von Neumann, not Hilbert. $\endgroup$
    – Gerald Edgar
    Commented Aug 4, 2022 at 15:56
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For my thesis I learned a certain collection of tools quite well (Hormander's machinery for solving $\bar{\partial}$-problems in several complex variables with control of the norm of the solutions in some Hilbert space). I learned the kinds of problems people had solved with these tools. I choose one problem which seemed tractable with this technology but which no one had tackled yet (concerning approximation of holomorphic functions on a domain by holomorphic functions on a slightly enlarged domain). This problem was too hard, so I introduced additional constraints on the problem until it was tractable. I think this sort of pathway is fairly typical. You don't go chasing the Riemann hypothesis: you learn the tools of the trade, and then push the boundary just a little bit.

Take this answer with a grain of salt since my research career ended with my thesis. I am much more interested in teaching. A more seasoned researcher or dissertation advisor might have a more informed take.

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This is the number one result on my Google search for survivor bias:

https://en.wikipedia.org/wiki/Survivorship_bias

If you want to do original work, some degree of initiative is required.
"Message to Garcia". Of course this doesn't mean NEVER to ask a question. But to not even Google, shows extremely low initiative. You ain't solving FLT with that ethic.

Also, yes, psychological hardening--although having nothing to do with survivor bias--is a benefit to doing R1 research. There's a lot of discouragements (including people issues) along the way.

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