I generally chase after whatever my adviser/supervisor tells me to do, although I know that it's sometimes a project that they don't want to spend their time on. I know that I can learn a lot even when I go after such "wild goose chases".

I recently talked to a PhD student though, and he advised me that I should learn when to say "no" to an adviser, to recognize that sometimes those suggestions can lead to "wild goose chases" that aren't worth the time.

What are some guidelines when an adviser wants you to chase a problem that might not be worth its time investment?

  • I modified the question slightly; please verify.
    – eykanal
    Commented May 24, 2012 at 0:00
  • 1
    Yes - that's perfect - thanks! Though I should modify it a bit since I'm not in the situation right now and don't want to give the impression of being in that situation (and certainly don't want to be embarrassed if my advisers find my posts here). Commented May 24, 2012 at 0:07
  • <comments deleted> Please do not use comments to post answers. Comments are here specifically to help improve the content of the post; not to answer questions. Thanks. Commented May 24, 2012 at 15:20

3 Answers 3


This will depend upon your relationship with your advisor. Does your advisor solicit your opinions on projects? Does he/she project openness about projects? Does he/she give you several options of projects? Does he/she ask for your suggestions?

If yes, then I think you can have a frank conversation with your advisor. Mention your concerns politely, and ask your advisor for their thoughts on those issues. Maybe your advisor has already given them thought and has some reasons to think it's a better project than you realize, and can explain to you. Maybe your advisor thinks highly of you and has handed you a long-shot high-risk high-reward problem, on the idea that you might just solve it, and if you do, you'll hit a home run. Or, maybe the concerns haven't occurred to your advisor and that might lead to a fruitful discussion about how to deal with the challenges, or might lead to a change in your project. It's also possible your advisor might have good advice about how to mitigate the risks you are most concerned about.

For instance, one piece of advice I got from my advisor was: be ambitious, reach high, but also design your research to "fail fast". Think proactively about what are the most likely ways that the research might fail, and then try to order your work so that if the project is going to fail, you discover that fact as quickly as possible. That's not always easy to arrange, but your advisor might have helpful suggestions for you.

If your advisor doesn't seem likely to welcome discussion about which project to work on, you can still raise these issues, but you may need to be even more deferential and careful about how you raise them.

Some things to avoid: Be very careful to avoid sounding like you are whining. Faculty put a lot of effort and thought into trying to find good projects for their students, and it can be very challenging (you want to find something that they have the skills to succeed at and that they have a chance of completing successfully; but on the other hand, you want to choose an ambitious project which if successful will lead to a good publication, which often means it is hard to know in advance whether the project will succeed or not). My experience is that many students tend to be a bit critical and "picky" about projects, so be careful not to sound ungrateful.

Also be careful not to be too arrogant. Your advisor probably has a lot of experience with research, whereas you are just learning. Therefore, your judgement may be a bit off.

Also, keep in mind that it is expected that many research projects fail. Therefore, you have to be willing to take risks and take on research projects where you're not sure whether you will succeed, and you have to give 'em a good try. You should expect that perhaps 50% of your research projects will be failures, or at least will succeed in the way you initially envisioned. If all of your research projects are a success, either you should maybe consider taking on harder problems, or else you are very lucky to have an amazing advisor.

Moreover, remember that it is important that any research project you take on relate to shared interests. You want the project to be something your advisor is excited about; if your advisor is unenthused, nothing good can come of it. So if you've noticed that your interests seem to be a different than the things your advisor is excited about, your advisor may be trying to thread the needle of finding something of mutual interest.

One last thought: if you think your project sucks, one constructive way to move forward is to try to identify a better research project and propose it to your advisor. If it is truly promising, and if it is in an area of interest to your advisor, he/she might get excited by your idea and encourage you to run with it. Just be careful: since you don't have as much experience as your advisor, you don't have as reliable a judgement about what constitutes a promising project and what doesn't.


This is a difficult issue to deal with. You are correct in stating that (in some disciplines) this can be a significant problem, but as a graduate student, it may be hard for you to argue your case that the project will lead to a dead end.

I see two possible solutions:

  1. If you have a good relationship with your advisor, speak with him about your concerns. He may admit that he's not sure where the project will lead, but he will likely be willing to give you the background as to why he's interested in the project, and where it will lead you. These types of projects are also good opportunities to ask your advisor to introduce you to collaborators with whom you can complete the project, as he's only tangentially interested.

  2. If your advisor likely won't listen to you, then put in the month or three to do the necessary background research to prove your case. Look up the references, research previous findings, contact others who have worked in the field. One of two things will happen: (1) you will change your mind, or (2) you'll build a strong case to present to your advisor as to why this research is not worth yours or his time. If at that point he still wants you to work on the project, then either he has political motivations or he's just being unreasonable, both of which are indicative of larger problems which you should deal with.

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    Usually proving that sth is impossible is difficult to... impossible. Commented May 24, 2012 at 9:47

The answer is far simpler than these. There is exactly one rule to follow: do what will get you to graduate sooner. If the problem your adviser has asked you to tackle isn't going to become a chapter in your dissertation, say "no". A good adviser will direct you in such a way that you make progress to defending your dissertation. A poor adviser will try to get as much cheap labor out of you as he can before your funding runs out.

Don't let your doctoral adviser take advantage of you.

  • 3
    I completely agree with the last sentence, but not the paragraph before it. You're assuming that the degree is the goal of a PhD program, but degrees are just administrative trophies. Focusing on the immediate task (finish the dissertation) instead of the long-term goal (build up experience and reputation as a productive researcher) is short-sighted.
    – JeffE
    Commented Jul 4, 2012 at 17:38

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