Choosing a PhD topic: fashionable or established?

I was recently asked my advice on choosing a topic for a PhD. In particular, I was asked what the current and likely future trends in information retrieval research were. On the point of picking topics based on current trends, my advice was, choose the established over the fashionable:

It is of course difficult to predict exactly what the hot topics in information retrieval will be over the next few years. There seems to be increased interest in user-focused studies; in aggregated search; and in Web 2.0 technologies (using Wikipedia, searching twitter, and so forth). However, what is popular as a research area for high-performing researchers and companies is not necessarily what is advisable as a PhD topic. A PhD is primarily an apprenticeship, and it is more desirable for it to be in an established than a fashionable area. Established research areas are of known importance, have well-defined theoretical and experimental foundations, abound with niche topics, and are slow moving. Fashionable areas, on the contrary, may turn out to be ephemeral, are still amorphous in methodology, tend to be focused on a few central questions, and move forward quickly. Thus, if you choose a fashionable topic as your research topic, you are liable to find yourself competing with the brightest researchers from the strongest groups and companies on questions that are rapidly solved or abandoned.

I don't think that the fashionable versus established question is the most important one in choosing a PhD topic; more important, it seems to me, is to choose a suitable supervisor and then choose a topic that fits that supervisor's interests and expertise. But to the extent that the choice between a fashionable area for a PhD topic and an established one is important, I favour the established option. What do other people think? Am I being too conservative?

7 Responses to “Choosing a PhD topic: fashionable or established?”

  1. vk says:

    sorry, but aren't established/fashionable somewhat arbitrary/subjective terms. For a newbie its not clear which fields are established!

  2. william says:

    Yes, that's true. That's why you need your prospective supervisor's advice! However, what you should be asking your supervisor is not necessarily, "what's cutting edge right now?", but "what is a suitable area for a PhD research project?" The two are not necessarily the same.

  3. FD says:

    I agree completely in theory, William. Although a solid thesis on an established area is important both for the student and the community, a thesis on a fashionable area is important at job-hunting time. Justifiably or not, fashionable areas are more exciting to hiring committees. It is very difficult to give an exhilarating presentation on MAP for the lay audience. That's not to say that every student should strive to make incremental improvements on old collections using incremental improvements on old methods. Some of this is necessary of course. But, if providing advice, I would recommend that a student find a new, under-explored, or weakly formalized fashionable area and approach it all of the machinery of the established area. Look at the fashionable area from the perspective of the established theories and methodologies and make sure it creates novel research questions. The thesis should ideally move forward the established while being exciting to the non-IR researcher. Make sure the thesis is explicit about both of these aspects.

  4. william says:


    Thanks for your comments. On reflection, I think that you're right, and that I'm being over conservative, cautious, and unambitious in my remarks. I'll ponder this some more.

  5. Stephen Jones says:

    Incrementalism suits those who seek a PhD without having acquired a passionate interest in some problem. Real advances are made by those who have identified a real problem and have a strong desire to do something about it. Of course, this the risky path, you may not succeed or you rattle too many cages. Excellent article in this vein :

  6. william says:


    Thanks for the link to the Ullman article (as it happens, he is giving a seminar at Melbourne this afternoon).

    My summary:

    Ullman decries a model of research in which topics are found by gathering open problems from existing papers, and the goal is to produce a new paper with its own open problems. Instead, research should be driven by real problems and the customers for their solutions (not "what can be solved" but "what needs to be solved"). Finding what needs to be solved is not straightforward. It cannot always be gleaned from existing papers. Industry exposure is valuable here; students should be encouraged to undertake internships at leading commercial research labs. A useful model is project-centered research. Set up and run a group project, and have student research feed off from that. (On this topic, see also David Patterson's article in the same issue of CACM, Your students are your legacy.) And if students find real problems that they think can best be solved by forming a start-up company, rather than finishing their thesis, then encourage them to do this. (Ullman was Google founder Sergey Brin's supervisor; Brin never completed his thesis.)

  7. Educator says:

    I cannot believe that you said the following:
    ....more important, it seems to me, is to choose a suitable supervisor and then choose a topic that fits that supervisor’s interests and expertise...
    Really? You should ensure there is a match in research interests way before then when you are applying to join a Ph.D. program. Isn't that part of what you write in the statement of purpose? Once you get into a program that has professors whose general area of research interest matches yours, then you pick a topic that you are passionate about. Something that you can research many years into the future because it excites you. What is fashionable or established shouldn't count for anything. It is your passion and interests that count for everything!!!!

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