Professors looking for PhD students will often have several ongoing research thrusts that students can work on. These may correspond to different three- or five-year grant awards, for example, or they may be different directions within the same grant.

In my cursory experience, watching various labs progress over a few years, I have found that some of these thrusts are very successful, resulting in high-quality publications, interest from the community, star students, and so on; whereas some (say, one out of every three thrusts) will fail, leaving the students who worked on that thrust discouraged and stagnant, and in many cases leading to them leaving the program, switching advisors, or (in the best case) switching to a different project.

My question is: as a prospective student, choosing a research project, are there any reliable warning signs or red flags to watch out for? What makes a project risky or safe?

There are many other factors to doing a successful PhD, in particular having a supportive advisor and a healthy department culture (see e.g. here). I'm not asking about those aspects, but rather the chance of research success of the project itself. This and this are related questions.

  • 1
    I could write a book on this one, but it would revive memories. Other things equal, pick a well-funded group and avoid groups where the PIs have short arms and low pockets.
    – Ed V
    Sep 2, 2022 at 21:42
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    Hmmm. If there were reliable indicators of failure up front, then there wouldn't be any failures. If you are tenured and secure then you can take on projects with no clear path to success.
    – Buffy
    Sep 2, 2022 at 22:04
  • @EdV Would love to read the book! Or just an extended answer :)
    – user162295
    Sep 2, 2022 at 22:22
  • @Buffy That makes sense. But are there really no warning signs at all? There are projects with varying levels of riskiness (all worth pursuing) -- what distinguishes the more "risky" projects?
    – user162295
    Sep 2, 2022 at 22:23
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    Probably both the projects that crash and burn and the projects that are very successful come from the same "high-risk" category, rather than different ones. Safer projects are more incremental and have both a low risk of "crash and burn" and a low ceiling. Ideally, advisors would not let their students fail merely because they spend some of their time on a high-risk project - other options include diversifying their work, starting on something more "sure" even if it isn't as flashy, etc.
    – Bryan Krause
    Sep 2, 2022 at 22:26

2 Answers 2


First of all, there is no such thing as a completely safe research project, at least one that is worthy to award a PhD for. The only way to know whether a research plan works is to perform it. This is simply because research by its nature explores the unknown – if we already knew the outcome of some piece of research, we wouldn’t have to do it anymore.

That being said, there are more and less risky projects (and also more and less risky fields). Usually, the more risky projects come with a higher reward if successful, while there is less or no reward for an unsuccessful project, even if done as diligently as possible. This is partially a problem of the scientific community not rewarding negative results as much as it should (see publication bias), but also partially due to a PhD signifying that you can complete a research project, which you simply don’t learn by exploring a hundred dead ends. Mind that another risk lies in how exciting the field finds your results and you won’t usually know that either before you tried to publish the research.

Some projects are obviously risky, e.g., consider a project with the following outline:

We have a great new idea how to measure X. We will try to implement this idea. If successful, we will investigate its performance and see whether it allows us to measure X better than established methods.

This project is obviously somewhat risky, because the new idea could spectacularly fail or perform badly because of something nobody has thought of yet. However, most risks are only apparent to somebody with experience in the field. Taking the above example again: How would you know whether implementing the idea involves a lot of fiddling, finding the right components, or not? Or whether nobody gives a damn about measuring X more accurately, but only more quickly or cheaply? Or whether if you are in a field which does not appreciate methods unless you find something new and exciting with it?

Now, if you are looking for a PhD position, you are likely not very experienced in the field yet. Thus, most of the times you have to rely on somebody else’s judgement, usually that of the prospective professor. And of course the professor can be overly optimistic, dishonest, or completely oblivious to the above (because none of the projects that made their career failed and they never had to think about this). So what can you do about this?

  • Look at the professor’s statistics of supervisee success and PhD duration. For an extreme example, if supervisees are either very successful or not at all, you clearly have somebody taking risks.

  • Ask senior or former members of the professor’s group: They should have an idea about how much risk their professor is entering and how aware and upfront they are about this.

  • Ask the professor. If they can only give a one-line answer on the risk level or contingency plans or are offended by the question, this is fishy. Mind that many funding organisations ask for a risk assessment or contingency plans nowadays, so if the position is third-party-funded, there is a good chance that they already had to thoroughly think about this. (Unfortunately, this can also mean that the professor has already trained how to sell a project as less risky than it actually is.) Mind that a good answer can also be something like: “If the project fails, we should know quickly. In this case, alternatives are available.”

  • In general, a third-party-funded project is safer because this usually means some peer reviewers in the field already assessed the risk. But mind that the assessment could also be ”very risky, but somebody should try it”. Also beware whether it was really your project that was assessed, not some larger scheme that includes your project. Ideally, you can get the grant application and evaluation up front.

Finally, I wish to clarify that there is nothing wrong about taking certain risks. As elaborated above, some are inevitable to research. However, I think everybody involved should know the risks they are entering.


If your research project has a predictable outcome, it is not good research. Research projects should not be without a chance of failure.

Choose something that

  • Is plausibly important if it has the desired outcome.
  • Will allow you to try something else afterwards.

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