Finding a topic
Work top down
When you start out, you just don't know which questions are interesting, which have been answered, etc. So you start broadly. Pick something that interests you and start reading. Let's use cross-country income gaps as an example. Rich countries are 25 times richer than poor countries. Why?
Start reading. Take notes on what you read. Organize your notes, so you understand the "tree of questions" in that literature. In our example, part of the tree may look like this: How important are capital, human capital, and productivity? Within human capital: how that this be measured? Why does it differ across countries? Within the measurement question: there is a Mincerian approach and a production function approach. Questions there: how can we measure inputs to human capital production? How can we estimate a production function? The point is to get from vague, broad questions to specific questions that one could potentially study.
Even a well posed question does not help you if you cannot find an advisor. Therefore, you need to focus on areas where someone on the faculty has expertise.
At the very start of your search, you should visit the websites of faculty members in your field of interest and read some of their recent papers. This will give you an idea of the range of topics that you can get support for. It will also give you feel for the techniques that each faculty member uses (e.g., theory, econometrics, computational modeling).
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.
Example: You decide to study the question: "How much does human capital differ across countries?" The literature basically has two types of answers.
- Mincer equations: Regress log wages on schooling for U.S. workers. Assume that workers with given schooling have the same human capital in all countries.
- Estimate a schooling production function. Estimate schooling inputs for a set of countries. Calculate human capital from the production function.
The Mincer approach is not credible because it must assume that workers with given schooling have the same human capital everywhere. The production function approach turns out to be very tricky. It is extremely hard to measure schooling inputs (parental time, school inputs, child study time, child abilities, peer effects, etc.) and outputs (adult wages?). The functional form of the school production function is unknown.
This leads to two project ideas:
- Try to improve the estimation of human capital production functions. Look for better data (existing studies did not use individual data - this actually would be a good project which has not been done at the time I am writing this).
- Try to measure human capital without estimating a production function. How can this be done? If one could observe the productivity of workers from different countries, that would work. This leads to the idea: estimate the productivity of workers from country x as the wages earned by U.S. immigrants from that country (Hendricks 2002 AER).
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.)
Use common sense. A fair number of good ideas are obvious with hindsight. Example: A large literature has studied the causes of cross-country income gaps. Many hypotheses were investigated: human capital, organization capital, trade, etc. But common sense tells us that institutions are important. The obvious evidence comes from divided countries (East and West Germany) and from the former Soviet Block. Strangely, it took a very long time for this idea to be explored in economic research.
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.
Make a serious effort to demolish your ideas.
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. Do this early. Do not wait until you have a model or (worse) a paper draft. One objection could destroy the entire effort you put into the project. Such as: "X has done that already in a 1955 paper" or "This does not make sense because of XYZ."
Be sure to try simple examples first. They sometimes reveal fundamental flaws in an idea or question. Example: You want to argue that schooling accounts for large cross-country income gaps. You think about a model in which human capital depends on schooling according to h(s) = h(0) * g(s). A back of the envelope calculations that this cannot work. To generate income gaps of, say, a factor 10, you would need h(12)/h(2)=10 (U.S. versus Uganda). Then the return to schooling would have to be enormous.
A similar advice applies to the implementation. You may have a good question, but not a good way of answering it. Don't forget common sense. A lot of papers go through sophisticated analysis of a model that just doesn't make common sense.
Motivation, Ideas, and Lack Thereof
A common problem with dissertation topics is lack of motivation or lack of an idea. I often see papers that extend existing work in minor ways without any good reason why that should be done. Often, these are extensions of field papers. Usually, these turn out to be a waste of time.
Relaxing an assumption does not make a paper. You need to convince people that it matters to attack a question in a more general way.
A paper needs an idea. It is easy to find good questions. It is hard to find good ideas. Do not waste time on a project until you have convinced yourself that the idea is worthwhile. A question is something broad like: "How important are productivity shocks for business cycles?" "Why does education differ across countries?" An idea is a specific approach to answering a question. Such as: Kydland & Prescott for the business cycle question.
Before you start working on the details, you should be able to explain in non-technical terms why your idea has merit. If you can't do that, chances are your idea is not important.
Writing a good paper requires that you really understand the literature. You should read a lot and think a lot. See my comments on specialization.
When you start reading about a subject, you will generate lots of ideas. Most of these are no good, but you won't be able to see this until you really understand the literature.
Defer the Details
I see a lot of students with half-baked ideas and fully worked out models. This is a waste of time. In most cases, don't write down a model until you can precisely state:
- What is the question?
- Why is it important?
- What is the approach?
- Why does the approach make sense?
- What is the potential punchline? To borrow from Lee Ohanian: How does your paper change the way I think about the world?
- How does it fit into the literature?
This, by the way, makes a good template for an Introduction. You cannot know what ingredients your model needs to have, until you can answer these questions.
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:
- 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.
- 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.
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:
- Your papers will lack depth. They may look superficially interesting, but experts will view your papers as missing the point.
- 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.
Communicating with your committee members (CMs)
Remember: your CMs don't think about your project all the time. They forget details between meetings. Therefore:
- Stay in touch regularly. Too many students show up with a completed paper that was written without any input from the CMs. They are then surprised when the CMs think that major revisions are needed.
- Have a short summary document ready. In particular, have a document with the model equations.
Prepare for each meeting. Summarize your progress and the issues to be discussed in a short document.
Documents should not be written in prose. Prose is a waste of time for the writer and for the reader. Use an outline format.
Respond to comments. Do not just ignore them. Again, a short reply document is useful.
Early on, write out a plan for the paper
- It should address the items in the intro.
- Be clear about what results you may get and what the contribution would be.
- Until you can clearly state the potential contribution of the project, don't spend any time on it.
Models are presented in a standard format:
- Describe demographics, preferences, endowments, technologies, market arrangements.
- State each agent's problem.
- Define an equilibrium.
Only when all of this is done are you allowed to analyze the properties of the model.
See also notes on writing.
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.