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!
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
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
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.
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.
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
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:
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
- 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?