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.
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. (i) 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. (ii) 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: (i) 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). (ii) 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. 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.
Depth
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. |