I read that "One difficulty with research problems is that it is hard/impossible to know if the problem is easy or not" or when it can be solved. So how a graduate-research student (i.e., PhD or MRe) knows what to pick as his/her work, and/or how can his/her professor 'predict' it? Because if one knows if it is possible or easy to solve then he/she likely knows also how to solve the problem, hence it is no longer an open question.

If professors can't decide the period of time a project to be finished, how they risk tuition paid by students or scholarships granted?

EDIT - My intention is mostly on Pure Mathematics.

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    Who says that they do? Commented Jun 13, 2015 at 12:30
  • @Nate Eldredge - TravisJ in math.stackexchange.com/questions/1323577/… . the last sentence is also from him (changed literally).
    – MKR
    Commented Jun 13, 2015 at 12:32
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    As TravisJ says, it is hard/impossible to know! So that means that professors often do not know when, or if, a research project will get results; they just have to guess, and often are wrong. Commented Jun 13, 2015 at 12:38
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    "Because if one knows if it is possible or easy to solve then he/she likely knows also how to solve the problem, hence it is no longer an open question." There is still the issue of collecting data. Are you talking about a purely theoretical field of research?
    – adam.r
    Commented Jun 14, 2015 at 3:54
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    In my own (recently completed!) PhD journey, my thesis was a moving goalpost. First I thought I would do work on generalizing the Ohsawa-Takegoshi theorem. I learned a lot of technology to digest the original proof, and poked and prodded to see if I could get any improvements out. None of my ideas ever panned out in this direction, but throughout the process I developed enough mastery of the underlying technology that I could prove some nice related theorems which were only tangentially related. Basically, follow your nose, but be open to new opportunities when they present themselves. Commented Jun 15, 2015 at 1:56

5 Answers 5


The interaction between student and professor should not be a one-shot set-a-problem. Instead, they should be talking frequently, often once a week, and adjusting the nature and direction of the project based on what is being learned during it.

The project starts with some idea, from either the professor or the student, that the professor thinks likely to lead to an appropriate outcome within the available time.

As time goes on, the student should come to learn more about the project than the professor, and be reporting progress or lack of progress. The professor should be continuously evaluating whether the current line will lead to a good result, and encouraging redirection if not.

I am sure my doctoral dissertation was not at all what my advisor would have expected when I started on the project - it was a result of things I learned during it.

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    The oft-repeated claim that "the student should come to learn more about the project than the professor" is not necessarily relevant, I think, and may set up unrealistic (while un-necessary) expectations/goals... Commented Jun 13, 2015 at 13:50
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    Actually, apart from technicalities, I've rarely seen a student knowing more about a project than his or her advisor, at least in my field. Commented Jun 13, 2015 at 14:04
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    It may well depend on the field and on the project. Commented Jun 13, 2015 at 14:52
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    This depends very much on the student, the professor, and probably the field. I more or less stumbled into my topic on my own as a result of answering a question that my Doktormutter brought back from a conference and realizing that I could do a lot more with the ideas. I never discussed it with her, except to let her know that I was producing results; she was a great cheerleader and got funding for me to present a lot of it at a major topology conference, but she was working on rather different things at the time, and I’m not entirely sure that she ever internalized the definition of ... Commented Jun 14, 2015 at 3:17
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    ... the property that I was studying! But she was the perfect adviser for me. Commented Jun 14, 2015 at 3:18

As alluded to in other comments and answers, I think part of the confusion here (and often in similar inquiries) is due to the notion that there is a well-defined "problem" that is either "solved" or not. Sure, there are "long-standing unresolved" very-specific questions that may admit yes-or-no answers, but, even then, in real life one makes partial progress on things. It's not all-or-nothing.

For that matter, often a very meaningful project can amount to "try to understand X better"... where X is a thing worth understanding better. Very amorphous, really. Such situations are exactly where an experienced person can have good hunches about incremental progress, and also be able to appraise the significance of various incremental advances.

This is why most theses, and most research projects viewed "in the small", do not have an easily-describable, easily-motivated goal. Indeed, in some cases the acquisition of sufficient technical savvy to understand the short-term goal is a project in itself, and it is often the case that "understanding the question" is sufficient to nearly have an answer.

From another angle: it can happen that a project is very plausibly feasible, but the execution of it would require considerable exertion. That is, the thing does not magically do itself. And one never knows with certainty what unexpected intermediate tasks may arise.


A good problem given to a Ph.D. student should split into a series of almost certain, quite certain, difficult, hard, and almost unachievable results. A question of the form "Problem XYZ might be solved using the following new approach. Try it!" is not a good problem, because after a lot of work you will quite likely get "No, this approach cannot work because ...". Such problems are better left for late postdocs or tenured researchers, who can afford to take risks. A good problem is more like "For all finite groups we expect the following. For abelian groups I can immediately sketch a proof, although filling in the details will take a few pages. For nilpotent groups you can probably proceed by induction. For solvable groups I still expect induction to work, although there are some problems with ... . In general you have to understand ... ." Furthermore both the student and the advisor have to be flexible to deviate from the original plan of work whenever there is a reasonable chance that something can be found in the neighbourhood.

However, although the advisor has the duty to minimize the risks involved with doing a Ph.D., he cannot eliminate them. I can only be certain that something works, if someone has done it, and then doing it is not a Ph.D. project anymore.


Professors/senior researchers typically do an educated guess regarding the time needed to solve a problem, based on earlier experiences with similar problems.

Of course, it is still a guess, and they can be wrong.

  • If a professor's guess is wrong, the PhD student will end with no results to publish. What about the student's money and time and of course degree?
    – MKR
    Commented Jun 13, 2015 at 12:59
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    @MKR: That is an inherent risk of doing a PhD. Anyone who wants to start a PhD should be aware of this risk, and be willing to accept it. It can be mitigated to some extent: if after some time the student is not making progress on the problem, then as Patricia Shanahan says, they can work on something different. Commented Jun 13, 2015 at 13:04
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    @MKR I see where you are going. But that is a completely different thing, one doesn't need to fully solve a problem to get a PhD, but you have to show enough progress (for example, solving subproblems that help with the main result). In fact, many PhD projects start with a very vague and open ended description, and as you progress, you will find where it leads to.
    – Davidmh
    Commented Jun 13, 2015 at 13:05
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    @MKR "If a professor's guess is wrong, the PhD student will end with no results to publish." Yes. You will be surprised to learn that in the real world, few things that are worth doing have guaranteed positive outcomes.
    – xLeitix
    Commented Jun 14, 2015 at 9:22
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    @MKR Sometimes, though, in other cases, what the student found in the process of finding that they couldn't solve the problem may itself be worthy of publication. At the very least, you've then saved other researchers the trouble of attempting the same things that didn't work. More likely, you've given them insight into better understanding the problem, allowing them to move closer to a solution (or, sometimes equally useful, proving one doesn't exist.)
    – reirab
    Commented Jun 15, 2015 at 15:37

As a professor, I act as a scout for every project my students are working on. I also help students separate the 'wheat from the chaff'. This ensures students do not bark up the wrong tree, go on a wild goose chase, and more importantly, telling me something is impossible because they lack knowledge or are lazy explorers. In addition, this allows me to have back-up plans should a direction fails to pan out. In general, similar to what another reader said, we know what SHOULD work, but the details are left to the student to sort out.

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