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There is an open math problem that I am interested in. There was a lot of progress in fully working out the problem in low-dimensions and progress towards sub-problems of the main question up until the 1980s, but it seems that the research activity has mostly stopped since then. Newer papers just essentially reiterate previous results.

A pretty well-known professor in my department also published a few papers on this problem in the mid-80s, so I reached out to him and told him that my thesis adviser and I are currently studying this problem. He confirms that his work on the problem is very old, so I'm guessing he hasn't done anything newer with the problem since his last papers.

The problem itself is known to be quickly intractable for higher dimensions, say, for n>5.

I'm taking his words as an indication that there is not much interest in this problem, and that I should probably abandon it and find another problem to work on, for my master's thesis.

Am I making the correct interpretation of this professor's remark?

Should I still stick with the problem, even though it might be true that it is not currently being actively studied?

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    Rather than asking us how to interpret the professor's words, a perfectly reasonable thing would be to send a quick follow-up mail where you ask more explicitly whether he thinks there's still interest in the problem. – Nathaniel Jun 7 '16 at 6:16
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    There was a lot of progress in fully working out the problem in low-dimensions and progress towards sub-problems of the main question up until the 1980s, but it seems that the research activity has mostly stopped since then — Uh-oh. Sounds like we're working on the same problem. – JeffE Jun 7 '16 at 12:45
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    Until you have tenure, and the respite from professional pressure that comes with it, you should probably always be working on something with a reasonable probability of producing usable results in a near-term timeframe. Absent a compelling and convincing new insight, working on old, open, unsolved problems should probably be side-projects that you're fine spending time on and getting nothing tangible done with...because there's a strong probability that this is exactly the outcome you will end up with. – J... Jun 7 '16 at 19:06
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    Unsolved problems from the 1980's are likely either very uninteresting or very difficult. – gnasher729 Jun 7 '16 at 21:35
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    @gnasher: Somewhat likely, yes. But that's a bit of a defeatist attitude. The highlight of my postdoctoral career was when I answered an unsolved question from the 1950's (from a paper written by two very famous mathematicians). Long story short: it turned out to be neither very uninteresting nor very difficult. I might not have the tenured position that I do now if I hadn't given it a try. – Pete L. Clark Jun 7 '16 at 21:41
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To my mind, there are two critical questions to ask here:

  1. Do you and/or your advisor have any ideas for making progress and/or any new results on the problem?
  2. In general, what does your advisor advise?

Regarding (2): In mathematics, the single most important role a thesis advisor can play is helping a student choose a good problem. Problems are good because of a combination of interest on the part of the student and the advisor, community interest, potential or actual applications, and perceived difficulty level (i.e., tractable but not trivial). Asking a bunch of random internet academics whether to attack this problem seems a bit weird to me: what does your advisor think?

Interregnum: I would like to respectfully disagree with @Wolfang Bangerth's answer. A problem which was studied in the past and on which many papers obtaining partial results were written is a problem of interest to the mathematical community. In my circles at least, solving longstanding open problems is at least as good as solving problems that were posed last year, because the older problems have a higher level of demonstrable difficulty. If the papers in question had been written, say, 80 years ago, then one might have some concern that no living mathematician cares about it (still, you can make us care by doing something sufficiently nice), but problems from 30 years ago that are still being mentioned in contemporary papers are likely to be viewed as having a strong pedigree.

Regarding (1): if you have some traction on this old, unsolved problem, it sounds like a great thing to work on...at least for a while, to see what happens. Conversely, if you have no ideas....tell me again why you and your advisor started studying this problem? Or rather: ask your advisor again.

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    solving longstanding open problems is at least as good as solving problems that were posed last year - in fact, usually better than – Kimball Jun 7 '16 at 6:05
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    Thanks so much for your answer, Professor Clark. I agree that it is a bit weird to ask this question. I assumed that I would get some very quick answers that say something like, "yes, you are mistaken, if you choose to work on problems that haven't been actively worked on since the 1980s, and you should focus on what's current". I didn't expect much more dialogue. Instead, I got way more detailed, well-thought-out answers that advocate for both abandoning the problem or trying to work on the problem. This was surprising :) Thanks also for your awesome comment to Wolfgang's answer. – User001 Jun 8 '16 at 2:20
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Based on your brief description, I'd say a more likely explanation for the lack of work on this problem is that people are stuck. Not that there's no interest in it.

Still, I wouldn't recommend this problem for a masters' thesis (or a PhD thesis). At least at the start, you should work on something manageable. If you hit a manageable problem or two out of the park, then you can start trying things professional researchers have attempted and failed.

  • Thanks so much for your answer @user37208 :) I am considering alternatives for my thesis work now, just in case. – User001 Jun 10 '16 at 3:56
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Am I making the correct interpretation of this professor's remark?

All you've told us about the professor's remark is "He confirms that his work on the problem is very old, so I'm guessing he hasn't done anything newer with the problem since his last papers." And what you said about your interpretation of his remark is "I'm taking his words as an indication that there is not much interest in this problem". While this may very well be a correct interpretation, there are certainly other possible interpretations. For example, I worked on problems 15 years ago that I no longer have any interest in. If a student came to ask me about them I would probably shrug and not show much enthusiasm, but those problems are still very interesting to many other people.

In other words, your description of the professor's remark (and possibly also the remark itself) is too vague to be able for anyone here to be able to meaningfully say whether the problem is still of interest to anyone or not. You and advisor might want to get a second opinion from another person who is knowledgeable on the subject.

Should I still stick with the problem, even though it might be true that it is not currently being actively studied?

I'm currently writing a paper on a problem from the 1960's that has been the subject of only very few papers since then, the last of them being from the early 1990's. I don't know for sure how the world will react to my paper, but I think I've made very nice progress on the subject and have hopes that my new results will excite new interest in the problem, which is intrinsically very appealing. I am also a tenured professor and can easily afford to risk the scenario where this doesn't happen. Nonetheless, I am of the opinion that pure math research shouldn't be about following fashions or fads (which math is very much susceptible to, much like other areas of academia) but should be driven by an innate desire to understand a structure one is interested in and finds beauty in. See also Pete L. Clark's comment on Wolfgang Bangerth's answer for examples where working on an unpopular or archaic subject paid off bigtime.

With that said, a lot of people prefer working on popular topics and think that working on such topics is a safer route to success in math, especially for someone who is just starting out. I don't have a strong opinion that that's false -- it's simply not my style -- and I completely respect someone who makes their decisions based on such a belief. So keep in mind that working on a subject no one else is working on is a somewhat lonely pursuit with a very uncertain payoff. But if that where your heart tells you to go, you should know that it is certainly possible to find success working on unpopular subjects.

  • Thanks so much for this awesome answer, Professor Romik, and best of luck to you with your upcoming paper! :) – User001 Jun 8 '16 at 2:08
  • This is my favorite answer. If your math has intrinsic beauty, people will notice. – Forever Mozart May 13 '17 at 1:26
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Being a researcher is, like anything else, a job. It's a great job, and (I assume from context that you're in mathematics) academia is literally the only place where you can work on nontrivial pure math. Unfortunately, in order to eventually get the awesome post as a university professor, you need to jump through the various hoops beforehand: publish a ton of papers, get prestigious postdocs, publish a second ton of papers, etc. If you don't do so, then you'll be stuck deciding working in insurance or finance. (Not that there's anything wrong with either, but I assume from the fact that you're doing a PhD in math that you'd rather be doing academic math research.) If you have what you think is a promising approach, go ahead and take the time to work on the project; resurrecting a moribund field and solving a problem that was thought to be intractable is a great feather in your cap. On the other hand, if you simply think that the problem is interesting but don't have a specific plan of attack, I'd suggest you work on something else instead.

Of course math and research are supposed fun and interesting, and they are. It's irresponsible, though, to suggest that you should simply work on whatever project you find most interesting. Being a grad student is a job like any other; your task is to churn out awesome papers. If you don't do that, then you won't be allowed to be a mathematician, and you won't have an opportunity to work on math at all. I'm not saying that grad school, post-docs, etc. should be a joyless slog; I am saying that you always need to keep in mind that this is just the preliminary stage of your nascent career, and that you need to consider that the ultimate goal is to move up the ladder. You need to show results. If this new project isn't generating results, dump it and get another.

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    This is certainly a valid point of view, but your answer assumes the premise that the problem in the supposedly inactive, abandoned area is in fact a less fertile ground for discovering exciting, groundbreaking research. The point that I was trying to make, and I think the point Pete L. Clark was trying to make in his comment and answer, is that it is far from obvious that that premise is correct. There are hidden diamonds lying buried and waiting to be discovered in long-abandoned areas, and someone who goes digging for them may find them, and has the distinct advantage that ... – Dan Romik Jun 8 '16 at 3:12
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    ... he/she is the only one looking. By contrast, when you work in a very active, "hot" field you have tons of competition, which could end up making it that much more difficult to be the first to discover those diamonds. So, there are pros and cons to both approaches. With that said, I completely agree that a student early in his career needs to be very mindful of the effect of research choices he/she makes on their career. But working on an old, abandoned problem can in certain cases be good for someone's career, and in that case honestly I don't see a problem. – Dan Romik Jun 8 '16 at 3:16
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    @Dan: What you say about my comments is correct. (And I agree with what you wrote.) – Pete L. Clark Jun 8 '16 at 3:48
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    @DanRomik: There's also the unavoidable fact that certain fields are sexier or in higher demand than others. If you're publishing great results in a field no one cares about, it's possible that no one will still care about it. Universities build up subfields in departments, and professors like people they've worked with. – anomaly Jun 8 '16 at 3:50
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There are two possible interpretations:

  • It may be that the problem is really just that hard that with the knowledge we have today, no progress can be made, and consequently no progress has been made in the last 25 years. If this is the case, it's probably a bad problem for you to work on as it seems rather unlikely that you will be able to squeeze useful results out of the general area (either for your personal satisfaction, for writing a thesis, or to build a research career on).

  • Or, it may be that simply nobody cares about the research area any more. There are many areas of the sciences that have been abandoned over the decades and centuries, simply because the circus moved on. There can be many reasons for this. In pure math (it sounds like this is your area), a possibility is that in the 80s people thought that working on question Q would open a way to prove open problem X in a certain way, but then someone found a completely separate approach to prove X, and so question Q has now lost its previous status and people don't care about it any more. Of course, if this is the case, you may be able to squeeze some results out of problem Q for a thesis, but it's again not a good problem to work on because nobody cares about it any more.

Upshot: If an area is dead, let it rest in peace.

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    "Upshot: If an area is dead, let it rest in peace." Hmm. If Robinson had followed this advice (calculus with infinitesimals), we would not have nonstandard analysis. If Mumford had followed this advice (classical invariant theory), we would not have geometric invariant theory. If Bhargava had followed this advice, he would have neither his Annals papers on counting number fields (Gauss composition) nor on average ranks of elliptic curves (geometry of numbers) hence probably not his Fields Medal. A student of math history can cite many such "fruitful resurrections." – Pete L. Clark Jun 7 '16 at 4:07
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    "[C]ome on, you surely know better." No. "The fact that there may be successful alternatives to the rule doesn't make the rule any less valid." That is literally the least scientific statement I have ever heard. Falsification is exactly what makes a proposed rule less valid! "[B]ut any student of math history will also point out equally many, or probably more, areas that are solidly dead, rightfully so, and for the better." I am a (part time) student of math history, and I am having trouble thinking of any good examples: especially of "for the better". – Pete L. Clark Jun 8 '16 at 15:49
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    What you are saying now is based on a strange fallacy for which you surely know better. Even after I mentioned one of the most recent Fields Medalists got his Fields Medal by not following your advice, you still want to regard that as an exception to be discounted. That doesn't make any sense: if some of our contemporaries are building amazing careers by not letting things "rest in peace," then obviously you should not always let dead areas rest in peace. It does not follow that you should never do it either: why do you have to give a categorical answer? You don't: that's a fallacy. – Pete L. Clark Jun 8 '16 at 15:55
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    @Yemon: Yes, I didn't say anything about beating the odds, taking big risks etc. In my answer, I recommend that the OP work on this old problem for a little while, if he and/or his advisor have any ideas. Otherwise not. I also hit pretty hard that it is an advisor's job to help their student work on problems with the right level of ambition and difficulty: students working alone would have a lot of trouble with this, and it is probably the thing that young-but-post-PhD math researchers struggle with the most. – Pete L. Clark Jun 8 '16 at 17:15
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    @Wolfgang: Your initial examples are of mathematical exposition rather than mathematical research. We don't even explain freshman calculus the same way today as we did 50 or 80 years ago...but the subject as viewed by a research mathematician has not changed at all. Quaternions and octonions are highly studied in contemporary mathematics. I regularly read and cite papers that are 50-80 years old. This week I read a paper from 1967 and one from 1935: the latter has a theorem that I will prove again in a paper I'm writing. So your comments really do not ring true to me. I'll end there. – Pete L. Clark Jun 8 '16 at 19:01

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