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.