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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. 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
are totally unrelated (although that's usually not efficient).
The
best approach is to not look for a topic. Just sit down and
try to understand the answer to a question. Yes: a question!
Good project ideas end with a question mark. Be suspicious
of ideas like "we want to explore..." 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 on 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 over samples guest workers. Perhaps one could use
that data to address the open issues? (This is actually a
project idea worth pursuing, not just a fictitious example.)
Disclaimer:
We are sure there are reasonable people who vehemently disagree
with our views on this. |
