I am working to get a PhD, maybe next year this time around. Currently, this is my second year. I have published 3 papers. All of them are not about one problem but consider different problems. My strategy to find a research idea/problem is given below.

1 - Read papers whose titles are either interesting or I have some apriori understanding of those titles.

2 - Understand those papers as best as I can. That is, I try to understand each detail presented in the paper except the simulation results (this is because I think simulation results are hard to reproduce).

3 - I analyze the paper and try to find a very small problem which can be addressed (i.e. I can solve it) by the methodology of the paper.

4 - If I am successful at step 3 I start working on that problem otherwise I repeat the process from step 1.

By applying this strategy I have been able to write 3 papers and I have submitted a fourth (I am not satisfied with those papers because at very best they can be considered average papers). But my concern is that the problems addressed in those papers do not belong to one area. As far as I have seen, for the profiles of some of the renowned researchers in my field their PhD work is focused on one area. One main thing I console myself with is that almost all of those researchers had good supervisors. My supervisor does not even read the draft/reviews of my papers and the suggestions that he provides during the meetings are so broad that the problem becomes intractable. Under these circumstances what are your opinions: Is there any better strategy to do research?

I will be very thankful to you for providing me suggestions or commenting on my dilemma.

3 Answers 3


This is a really important question, and it's one that isn't asked enough.

From reading your question, though, it sounds like you are rushing a bit. Renowned physicist and biologist Uri Alon (34k+ citations) has written an excellent paper on 'How To Choose a Good Scientific Problem' and one of his main points is that one, however cliché it sounds, should take ones time to conceive a good project.

I strongly suggest you read his paper. It's not exhaustingly long, and reads like a good talk. He also has a TED talk that challenges the 'A to B' dogma in science, which has helped me a lot.

  • what would you comment on my strategy? Do you find it common or is it not a good strategy at all? Commented Jun 24, 2016 at 8:20
  • What field are you in? How much time do you have left of your PhD? How many papers are you required to publish? I'm not in a position to give an ultimate statement of what is a good strategy or not as a strategy should always suit its environment, but if my opinion has any value, I observe that the best research does not come from scavenging existing literature for holes and trying to cover them. Try instead to reflect on deep questions that arise from some of the best papers you read and weigh their research feasibility with the possible knowledge gain from pursuing them (see Uri's paper).
    – Ulf Aslak
    Commented Jun 24, 2016 at 8:31
  • Thanks for your comment. BTW my field is wireless communications and almost one year is remaining in my PhD. The requirement for PhD is 2 SCIE paper which I have already published but as I mentioned in my OP that those papers are not really good papers even in my own eyes. Commented Jun 24, 2016 at 8:45
  • 1
    In your position, you have already done "the things you have to do". If your superviser is as disinterested as you explain, I suggest you take advantage of that and pursue something that you find interesting albeit riskful. The worst that can happen is that you can't publish your final efforts because it led to a dead end, but you still get your PhD. At best, however, you discover something new and interesting at your own merits.
    – Ulf Aslak
    Commented Jun 24, 2016 at 9:21
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    Thanks for the pointer to Uri Alon's article. It's a very friendly read as you said, and is very helpful!
    – Tripartio
    Commented Jul 6, 2016 at 1:09

Generally finding good problems you can solve is not easy, and in my view it's one of the most important abilities of good researchers. Personally, I spend a lot of time thinking about what is interesting to me and what I want to be working on. Then I end up only having time to think about a small portion of that.

I don't know about your field, but in mine, it's hard for young (and even some not so young) people to figure out both (1) what are interesting problems, and (2) what are doable problems. Your approach could result in good problems, but it also sounds a bit haphazard and might not. It's good to get input from other experts. Here are a couple concrete suggestions:

  • Go to as many conferences/workshops/summer schools/seminars/etc you can. This way you can meet people, see what they're doing and see what they think about what you're doing. This way you get a better sense of the field and current research, and if your lucky someone might be able to suggest a good problem to you.

  • Look for another advisor. It sounds like your advisor is not giving you the support you want (note: some advisors are hands-on and some are hands-off; hands-off is not necessarily bad). Maybe it's too late to find another primary supervisor, but maybe you can either get a co-advisor or get an unofficial advisor for a new project. Of course you should make sure your current advisor won't have serious issues with this and frame it in the right way (e.g, "I was talking with Prof Y about ABC. What do you think about me working on that?").

  • I have seen the suggestion that one should go to conferences for learning about what people are doing. If conference papers are available online even then is it important to go to conferences? Actually, I have never attended a conference hence i am wondering if papers is the only thing that are presented in them then we can access those papers online. Why do we need to attend them? Commented Jun 24, 2016 at 17:50
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    @FrankMoses One of the most important aspects of conferences is meeting and talking to people. In my area I would take it as a sign you are not really interested in research if you don't go to conferences. It's also harder to get an academic research job if no one in the field knows you.
    – Kimball
    Commented Jun 25, 2016 at 0:15

I feel that if you want to survive in academia and climb up the ladder, you need credibility in the community, which gets somewhat hurt by your step no 3 ( I am assuming you are not being modest like some super-genius people I know, by calling your papers average). Because, as you said you are using their "methodology", so people will eventually know that. Ideally you should start with a big question, then narrow it down to some level and then pick the papers accordingly to know the state of the art. The "question" is really important and it is very hard to formulate a good one. Therefore, I would suggest to focus on this part.

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