Finding a topic

The best approach is to not look for a topic. Just sit down and try to understand how the literature answers a question of interest. Yes: a question! Good project ideas end with a question mark. Be suspicious of ideas like "we want to explore ..." Be very suspcious about ideas like "what happens when feature x is added to a model?" You need a question.

Anyway, at some point you'll get the idea of what others think about the question of interest (or even of what interesting questions in a given area may be). Then simply ask: "Do I believe what I have read? Is it convincing?" Forget the fact that you are looking for a project. Just ask whether you believe what you have read. You will typically find that there are many shaky issues in the proposed answers. That's where an idea is born. If you find something that is really unconvincing, it is an opportunity to do better.

Of course, in most cases it will simply be too hard to do better. Then you don't believe that the existing findings are bullet proof, but they are still the best answers available. It is useful to keep these kinds of situations in the back of your mind. Perhaps you'll see something later that allows you to follow through with your idea after all.

Example: The migration literature argues about immigrant quality and earnings of immigrants relative to natives. But it's very hard to figure out what's really going on in all the data because we don't have longitudinal observations. So there is a clear potential for improvement, but it's not feasible because the data don't exist. Write that down. Later on you find out about the German Socioeconomic Panel and the fact that it oversamples guestworkers. Perhaps one could use that data to address the open issues? (This is actually a project idea worth pursuing, not just a ficticious example. In fact, recently a number of papers using longitudinal immigrant data have come out in top journals.)

What happens once you have found a candidate topic: Try to convince yourself that the idea is no good. This is important. Before you sink any time into an idea, make sure it is worth it. Most ideas are not worth anything. There are many reasons. Perhaps the idea is too marginal. But more commonly it is outright flawed. Make a list of objections against your idea. Be sure you know how to respond to them. Talk to people and ask them for objections.

One more suggestion: Work on a topic that at least one local faculty member knows in detail. Otherwise, it will be hard to convince your committee members to spend a lot of time on your project. And the comments you will receive may be far off the mark.

To plan or not to plan?

Some people ask: "what is your research agenda?" Ideally one could answer: "I want to understand this big picture question and here are the steps that will get me there ... At the end I should have the following papers ..."

If that works, great! It usually doesn't (take a look at Parente and Prescott Barriers to Riches for a great example where it did work). There are at least two reasons:

1. Until you have actually done a step in the plan, you typically have no idea what will come out (especially if the work has any empirical content). But what comes next depends critically on what you found before.
2. It is hard to come up with a good idea/question that can actually be done. It is darn hard to come up with a whole sequence of such ideas at a time.

Therefore, be realistic and take project ideas one at a time. Think of each dissertation chapter as one publishable paper. Don't try to write a monolithic dissertation where one chapter leads cleanly to the next. It's perfectly fine if your chapters address different questions.

But: At any cost, avoid working on several unrelated problems. To be successful, you must specialize. Each time you work on a new topic, you incur the large fixed cost of really, deeply understanding the literature. It is therefore essential to zero in on one or two areas and then stick to those for several years. If you do not follow this advice, you will encounter two problems:

1. Your papers will lack depth. They may look superficially interesting, but experts will view your papers as missing the point.
2. When you try to publish your work, you will have to convince referees that you should be taken seriously. They need to know that you have published in the same area before.

Aim to associate your name with a topic. If you work in many different areas, nobody will know who you are. But if you persistently work in one area, people will hear your name and immediately think: "he/she works on X." This is how your work is taken seriously and how to get impact.

Disclaimer: I am sure there are reasonable people who vehemently disagree with my views on this.

Theory vs. Empirical Work

Theory is glamorous and in many respects just more interesting and more fun to do than data work. If you doubt that, start reading the documentation for the PSID. Data work involves a lot of tedious steps and a lot of time during which essentially nothing is learned (except about the twisted minds of those who publish data sets). If you doubt that, start reading the documentation for the PSID. 

And yet, you should consider doing empirical work. For one simple reason: It may get you a job. There are loads of theorists coming out of top departments every year. The best of them get jobs. The others often have a hard time because the market for pure theory is not that large. Having an empirical project or at least a serious empirical part in your dissertation immensely increases the range of jobs you can apply for.

There is unfortunately a big barrier standing between graduate students and data: Empirical work is hardly ever taught. The first time around, the startup investment required for using a data set is very large. If you doubt that, start reading the documentation for the PSID. Which is why many grad students never touch any data. But this obstacle can be overcome through persistence.

Romer's Rules for a Dissertation

• Don't clutter up your life with other activities; just write.
  
• Don't carry out a thorough and comprehensive search of the literature; just write.
  
• Don't attempt to make sure that every page you write shows the full extent of your professional skills; just write.
  
• Don't write a well-organized, well-integrated, unified dissertation; just write.
  
• Don't think profound thoughts that shake the intellectual foundations of the discipline; just write.
  
• If you don't have a paper started by the spring of your third year, be alarmed.
  
• If you don't have a paper largely drafted by the fall of your fourth year, panic.
  
• Have three new ideas a week while you are getting started.
  
• Don't try to game the profession, work on what interests you.
  
• Good papers in economics have three characteristics:
  • A viewpoint.
  • A lever.
  • A result.

Another disclaimer: I'm not sure I agree with even half of Romer's points.

To Ph.D. or not to Ph.D.?

Finally, a word for those who are considering whether or not to apply for a Ph.D. program:

If you are not sure you want a Ph.D., do something else.

The Ph.D. program is structured with a single outcome in mind: to place graduating students as faculty in Research I universities. The material learned is useful for only one purpose: for publishing research in academic journals. It is not useful for consulting, for working in businesses or the government (other than the Fed), or even for teaching. Therefore, if you are not sure you want to do academic research for the rest of your life, do not apply for Ph.D. programs in economics. An MA or an MBA always has a higher payoff and will save you years of frustration.