Finding Thesis Topic

Generally speaking, a good Ph.D. thesis topic is interesting to you, toyour advisor, and to the research community. As with many aspects ofgraduate school, the balance you find will depend at least in part onthe relationship you have with your advisor. Some professors have welldefined long-term research programs and expect their students tocontribute directly to this program. Others have much looser, but stillrelated ongoing projects. Still others will take on anyone with aninteresting idea, and may have a broad range of interesting ideas tooffer their students. Be wary of the advisor who seems willing to letyou pursue any research direction at all. You probably won’t get thetechnical support you need, and they may lose interest in you when thenext graduate student with a neat idea comes along.
　　
　　If youpick a topic that you’re not truly interested in simply because it’syour advisor’s pet area, it will be difficult to stay focused andmotivated -- and you may be left hanging if your advisor moves on to adifferent research area before you finish. The same is true forchoosing a topic because of its marketability: if you’re not personallyexcited about the topic, you’ll have a harder time finishing and aharder time convincing other people that your research is interesting.Besides, markets change more quickly than most people finishdissertations.
　　
　　In order to do original research, you must beaware of ongoing research in your field. Most students spend up to ayear reading and studying current research to identify important openproblems. However, you’ll never be able to read everything that mightbe relevant -- and new work is always being published.
　　
　　Tryto become aware and stay aware of directly related research -- but ifyou see new work that seems to be doing exactly what you’re working on,don’t panic. It’s common for graduate students to see a related pieceof work and think that their topic is ruined. If this happens to you,reread the paper several times to get a good understanding of whatthey’ve really been accomplished. Show the paper to your advisor orsomeone else who’s familiar with your topic and whose opinions yourespect. Introduce yourself to the author at a conference or by e-mail,and tell them about your work. By starting a dialogue, you will usuallyfind that their work isn’t quite the same, and that there are stilldirections open to you. You may even end up collaborating with them.Good researchers welcome the opportunity to interact and collaboratewith someone who’s interested in the same problems they are.
　　
To finish quickly, it’s usually best to pick a narrow, well definedtopic. The downside of this approach is that it may not be as excitingto you or to the research community. If you’re more of a risk-taker,choose a topic that branches out in a new direction. The danger here isthat it can be difficult to carefully define the problem, and toevaluate the solution you develop. If you have a topic like this, ithelps a lot to have an advisor or mentor who is good at helping you tofocus and who can help you maintain a reasonably rigorous approach tothe problem.
　　
　　In the extreme case, if your topic is so out ofthe ordinary that it’s unrelated to anything else, you may havedifficulty convincing people it’s worthwhile. Truly innovative researchis, of course, exciting and often pays back in recognition from theresearch community -- or you could just be out in left field. If youhave a far-out topic, be sure that people are actually *interested* init, or you’ll never be able to ``sell’’ it later, and will probablyhave trouble getting your work published and finding a job. Inaddition, it will be hard to find colleagues who are interested in thesame problems and who can give you advice and feedback.
　　
　　Inany case, a good topic will address important issues. You should betrying to solve a real problem, not a toy problem (or worse yet, noproblem at all); you should have solid theoretical work, good empiricalresults or, preferably, both; and the topic will be connected to -- butnot be a simple variation on or extension of -- existing research. Itwill also be significant yet manageable. Finding the right size problemcan be difficult. One good way of identifying the right size is to readother dissertations. It’s also useful to have what Chapman [chapman]calls a ``telescoping organization’’ -- a central problem that’ssolvable and acceptable, with extensions and additions that are``successively riskier and that will make the thesis more exciting.’’If the gee-whiz additions don’t pan out, you’ll still have a solidresult.
　　
　　Remember that a thesis is only a few years of yourwork, and that -- if all goes well -- your research career willcontinue for another 30 or 40. Don’t be afraid to leave part of theproblem for future work, and don’t compare yourself to seniorresearchers who have years of work and publications to show for it. (Onthe other hand, if you identify too much future work, your thesis won’tlook very exciting by comparison.) Graduate students often pick overlyambitious topics (in theory, your advisor will help you to identify arealistic size problem). Don’t overestimate what other people havedone. Learn to read between the lines of grandiose claims (somethingelse a good advisor will help you to do).
　　
　　Some schools mayrequire that you write a thesis proposal. Even if they don’t, this is agood first step to take. It forces you to define the problem, outlinepossible solutions, and identify evaluation criteria; and it will helpyou to get useful feedback from your advisor and other colleagues.Writing a good thesis proposal will take up to several months,depending on how much background work and thinking you’ve already donein the process of choosing the topic.
　　
　　The proposal shouldprovide a foundation for the dissertation. First, you must circumscribethe problem and argue convincingly that it needs to be solved, and thatyou have a methodology for solving it. You must identify and discussrelated work: has this problem been addressed before? What are theshortcomings of existing work in the area, and how will your approachdiffer from and be an improvement over these methods?
　　
　　Presentyour ideas for solving the problem in as much detail as possible, andgive a detailed plan of the remaining research to be done. The proposalshould include, or be structured as, a rough outline of the thesisitself. In fact, unless your final topic differs significantly fromyour proposed topic (which many do), you may be able to reuse parts ofthe proposal in the thesis.
　　
　　You will probably have to takean oral exam in which you present and/or answer questions about yourproposal. Be sure that your committee members are as familiar aspossible with your work beforehand. Give them copies of the proposal,and talk to them about it. During the exam, don’t panic if you don’tknow the answer to a question. Simply say, ``I’m not sure’’ and then doyour best to analyze the question and present possible answers. Yourexamining committee wants to see your analytical skills, not just hearcanned answers to questions you were expecting. Give a practice talk toother students and faculty members. Remember: you know more about yourthesis topic than your committee; you’re teaching *them* something fora change.