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grad skool rulz #10 – the dissertation topic

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Fabio

After exams and choosing your committee, the next big step is your dissertation – a lengthy project on a topic of your choice. It’s a crucial decision because your career depends on completing the dissertation and publishing from it. As usual, there is no perfect choice. There are trade-offs in choosing any topic.

Let’s start with a basic question – where do you get ideas? Here’s a couple of sources:

  • Big obvious problems – These are well known problems in most areas. For example, in population studies, a big question is when birth control becomes a widely accepted practice, leading to plunging fertility. Pro: You’ll be a star if you make progress. Con: Big, unsolved problems are big for a reason – they are hard. You might end up with nothing.
  • You invent your own problem – You identify an unanswered question based on your own understanding of a field. Pro: This can lead to some creative, engaging stuff. Cons: You may be seen as weird or irrelevant.
  • Your adviser gives you a problem – It’s common for advisers to have “problem lists” for people to work on. Variant: you work on the adviser’s project and get a piece of the action. Pro: Senior advisers usually have a good sense of what’s important in the field and what’s a tractable issue. Con: You may be seen as unoriginal and derivative of the adviser.

Other issues that are worth considering:

  • Passion – You had better like your topic because you might be working on it for years. It has to be something you can stick with in the face of skeptical advisers, relatives, editors and students.
  • Compatibility – Choose a problem that fits your intellectual style. If you like models, then choose something more mathematical. If you can do narrative, choose qualitative research.
  • Difficulty – Don’t choose a very simple problem, or one that is beyond your scope. If you tackle a tough one, get the skills that you need.
  • The research cycle – If you move first, you will get a big pay-off. Come last, and you will be seen as an imitator. Come way too early, people may literally not understand what you are talking about. Example: Social capital – super hot in 1995, not so hot in 2005, unless you have a really original insight.
  • Solvable – You have to have a realistic approach to tackling the problem. Time travel is a great problem, but no one has any idea about how to solve it!
  • Size – If you completely succeeded, how big would the result be? You don’t need to write a Nobel prize winning result in your dissertation, but you need to show that you are on track to bigger things.
  • Novelty – There is safety in numbers, but if you are too similar to other researchers, then you won’t get much reward. If you are too original, then no one will get your point. So learn to strike the balance.
  • Popularity – The topic needs to be able to attract the attention of the academic audience you wish to target. Remember, proving Fermat’s last theorem won’t get you points in the soc program!
  • Publishable – Is this something that might appear in the journals/presses that figure prominently in your area?
  • Time horizon – Can you solve the problem within a reasonable time limit? Unless you are willing to incur serious personal costs, any project that takes more than 2-3 years should be avoided by graduate students.

As you see, you will almost certainly have to sacrifice along some dimension. For example, an easier problem (low difficulty) may already have been addressed, which means you will be on the tail end of the research cycle (very bad). By considering these issues, you will make an informed choice that can help you get the most out of the dissertation process.

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Written by fabiorojas

May 20, 2007 at 7:47 pm

8 Responses

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  1. i think another thing to consider is how open-ended the research is. if a grad student is not highly self-motivated and self-disciplined, grounded theory is a recipe for spending a few years in the field before dropping out once they seriously face the prospect of sitting down and inductively analyzing their gigabytes of field notes. in contrast, it’s much harder to get lost with research where in the prospectus itself you can clearly plot out where you’re collecting data and how you’re analyzing it, right down to which betas test which hypotheses.

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    Gabriel

    May 21, 2007 at 8:31 pm

  2. Good point Gabriel – This leads to the “know thyself” principle. Self-starters can deal with open endedness. A good committee can point out the need to have a concrete plan, especially if the student needs structure. That’s why I alway encourage students to, if possible, include some preliminary results.

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    Fabio Rojas

    May 21, 2007 at 8:59 pm

  3. I’d add that the ideal dissertation should be important and, more crassly, marketable no matter how the results turn out. And, like it or not, the discipline values positive results more than null results. If there’s a chance that your star explanatory variable or mechanism will turn out to be a wash, it had better be the case that this null result is both robust and unexpected.

    This doesn’t mean, incidentally, that the diss has to address a new question. In fact, one of the most “successful” dissertations in the past 10 years, Pager’s audit study on racial discrimination, looked at an old question (“is there discrimination in low-wage labor markets?”) and generated an answer (“yes”) that few sociologists found at all surprising. But because she used a method that is relatively new to sociology and doesn’t suffer from the same problems as more conventional methods, she has been able to get a lot of mileage out of her research. Note that her diss would have been just as marketable, albeit more controversial, if it *hadn’t* turned up evidence of discrimination.

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    anon

    May 21, 2007 at 11:19 pm

  4. “This doesn’t mean, incidentally, that the diss has to address a new question. In fact, one of the most “successful” dissertations in the past 10 years, Pager’s audit study…”

    I think Fabio has this covered. It is a variant of “big obvious problem.” But I do think you have tapped another important dimension of a “sucessful” dissertation that Fabio overlooks…the end result should be interesting (to someone other than you) whether the null hypothesis is rejected or not.

    This is another reason that “big obvious problem” is a good starting point. Think of the legions out there teaching Sociology 101 and scrounging around for a different way of saying the same thing for the 500th time (e.g., “discrimination exists”) and you can understand the sucess of your example. If it hadn’t panned out, she would be sitting even more pretty as a “fellow” at AEI or a vetter of Justice Department apps for the Al Gonzales…literally a no-lose project. Why? Big Obvious Problem that lots of people care about.

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    dissertater

    May 22, 2007 at 11:38 am

  5. […] Some people I know are starting to think about their dissertation topics… maybe this will help them. […]

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  6. […] the science of organization and management writ small. It is also a key internal component of the Grad Skool Rulz. Thus, for deskbound workers of all sorts, tools and systems to enhance one’s productivity […]

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  7. […] the science of organization and management writ small. It is also a key internal component of the Grad Skool Rulz. Thus, for deskbound workers of all sorts, tools and systems to enhance one’s productivity […]

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