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Pick Your Poison

You might think that there are an infinite number of ways to choose a thesis topic, and to some extent, you would be right. Each student comes to graduate school with a slightly different mix of skills, interests, and goals. The same is true of every advisor. There is no formula for matching the two up and getting them to agree on a single research project--each pair has to find their own way.

But some themes recur in the experiences of all grad students. I conducted an informal poll of Ph.D. recipients in the sciences and asked them how they chose their thesis topic. When I read through the stories, they split into two distinct camps: Those who chose a research topic and then convinced an advisor to guide them to a complete thesis, and those for whom the advisor chose a project. Most people use a mix of the two, but one method always seems to predominate. Which style you select doesn't seem to predict whether or not you will finish, but it does seem to affect how you will feel about your completed thesis and how the scientific community receives your work.

I, for example, fell firmly into the "pick your own" camp. While working on a small project chosen by my advisor, I noticed a certain unexplained phenomenon during a lecture by a visiting professor. It occurred to me that this phenomenon might be caused by a process that I had come across in the course of my other project. Thinking it might be a good thesis topic, I brought the idea to my advisor's attention. A few simple calculations convinced us that the idea had merit, and it did eventually turn into my thesis.

But there were drawbacks to this approach that I hadn't considered. Although I was extremely proud of the work and it was praised by many of the field's cognoscenti, it was rarely referenced in any other papers. The problem is that it didn't build directly on any of the major research directions in my field at the time. So if you do come up with an idea of your own, it is worthwhile to spend some time figuring out if anyone else will care (see sidebar).

People in Your Neighborhood: The Advisor's Advisor

Science has a genealogy. Josephus begat Baltharius begat Agganezzer and so on down to your advisor's advisor who begat your advisor who will soon, if all goes well, beget you. The influence of your scientific ancestors may be obvious (you all study crocodile eyelids) or obscure (Q: Why did the biologist advise a mathematician to advise a computer scientist? A: bioinformatics!), but either way, it is always there. Although you may never meet your grand-advisor in person, keeping them in mind can help you understand how the scientific community views your research.

One way to test the relevance of your topic is to ask yourself (or them) if your advisor's advisor would be interested in it. They are the ideal person to use for this test because they are almost certainly still active in the area that you work in, but they are unlikely to be aware of your daily progress. Instead, they will follow your career like any other peer, through publications and occasional face-to-face meetings. And, like their peers, they have short memories, they don't have much free time at meetings, they don't read outside their field, and they are most interested in research that relates directly to their own work. So if you want your advisor's advisor to stay up to date on your work, you must publish regularly, develop a short-but-sweet summary of your current work to tell at meetings, and keep your research focused on one topic in your field of choice.

A good friend of mine, on the other hand, selected his thesis topic from a list provided by our mutual advisor. In many ways, our two projects were very similar--same advisor, same field, similar methods--but my friend's thesis remains a regularly referenced work in our field. As he says, "Even if they don't read it, they still reference it." The difference is that my advisor had a better sense of which direction the field was headed and what problems needed to be solved to get it there. So the project he chose for my friend was certain to be interesting to the broader community. But that approach also has its share of pitfalls. "That was my 15 minutes of fame as a scientist, but I always felt like I couldn't take credit for that," says my friend, "It was [our advisor] who chose the right topic at the right time."

Regardless of who ultimately chooses your topic, one thing is certain. You won't find a topic by daydreaming. So if you don't have a topic yet, get to work! Talk to everyone in your department about what they are working on, what they are trying to accomplish, and what sorts of problems they think need to be solved. Attend seminars in your field and listen for statements like, "We suspect that such-and-such happens, but no one has worked it out yet." And if you are one of those rare predissertation grad students who has an opportunity to go to a conference, take it and do the same thing there. The goal is to learn as much as you can about what people are interested in at the moment.

As you begin to get a sense of where you want to go with your research, or if the opposite happens and you begin to feel like you have no idea what to do, sit down with your advisor and hash it out. Ask for ideas and pass on your own. And trust your instincts. If a topic sounds boring, it probably will bore you. If it sounds exciting and you can't wait to run off and start working, that's probably the topic for you. But before you get too far, make sure you and your advisor agree on two things: the project can be done in a reasonable amount of time, and that no one has done it before. (Or is doing it! This may be impossible to figure out, since most people keep their work under wraps until it is done. But your advisor may have heard something over tea at a conference. ...)

Now you have a school, an advisor, and a research topic. Time to get down to work. But maybe you should read another article first? Sharpen your pencils? Get a drink of water? NO! Now is not the time to procrastinate, although virtually every grad student does at this point. The reasons are obvious. You are faced with a huge multiyear research project that may or may not work out well, but will certainly consume your every waking moment. It's intimidating. It's daunting. It's time to talk about time management.