Why is Research Difficult for Beginning Ph.D. Students?
Part of the difficulty with research at the beginning is that (a) it
is never a burning thing - you can always do it tomorrow, and (b) it
is not clear (at least before you complete a couple of research
papers) what needs to be done and where you're supposed to start. This
is why it is not very surprising that many students do not come up
with revolutionary ideas and get quite frustrated in their first
one-to-three years in the Ph.D. program -- very few such ideas come in
In that respect, you, the reader, should definitely not feel that
you're not up for research/Ph.D just because you did not come up with
any bright idea yet. It just takes determination and some guidance,
especially in earlier stages, and especially if you did not have the
experience in individually-led research. Determination is the name of
the game, which is why it is very important that you know and
understand why you're doing the Ph.D. The answer could be as simple as
"I enjoy research", or "I want to be a Professor at UIUC", or "I want
to get higher in industry", or "I want something more interesting in
life", or "I'm afraid to be a mediocre small screw in a large
industry". If you know why you're doing it, it makes it much easier to
be determined and focused in what you do.
So you are determined. Guidance is what you're missing more acutely now.
So, you should go to a random professor (not so random - after all,
you chose this school for your Ph.D., so you should have wanted to
work with some of those professors, and had a gut feeling about some
of them), ask her/him if s/he would be interested in working with you.
Many would say "work with me during my class, and we'll see", unless
you have exactly what it takes to work with them (knowledge,
and have proven yourself in research.
How long does it take to do a Ph.D.? How much time before ideas
just pop into my head?
Students differ, and it is typically not the problem of background
knowledge (although lack of background knowledge in your
goal-expertise area does not help). As I said above, the problem is a
little guidance (as a beginning Ph.D. student you don't know how to
answer a scientific question yet, not to mention asking the
question). Part of the guidance initially is in the advisor giving you
a question and some guidance on how to go about solving that question.
About thinking up new papers...
You need determination and stamina here. You see, each paper is a work
of "depth", i.e., asking the questions as you go instead of accepting
the answers that other people supply. For example, think about your
typical class project, one of those that you've done in the past year
or two or three. Many of those project include at least one good
question. Typically that good question is not the topic of the
project itself (although some of those are also interesting and cute
questions). The good questions are hidden in the assumptions that
you made in order to solve that semester-long project.
For example, consider the game of Poker. Trying to write a Poker
playing game is an interesting and cute problem. This is a nice
term project, one of those things that you could do in a term or
less. The interesting question, however, is not the game itself
but rather the assumptions that you make in solving the problem.
For example, the question of how you reason about someones beliefs and
knowledge. Now, you say, how would I even start to think about
reasoning about knowledge? Ah, you now see why you did not see the
question from the original Poker project. You made the assumption that
nobody worked on this before you, and that you are a little impatient
and just want to be over with that term project.
Why is knowledge about knowledge more important than Poker (I
mean, you could make a lot of money if your Poker algorithm
works well)? Well, from a scientific perspective you can build
on answers to the first and not the second. "Build what?", you
say. Well, first, you can build your Poker agent, but you could
also build agents for other games, advance economic theories on
the stock market and its dependence on information, and build
programs that understand humans' requests better (e.g., in a
computerized customer-service agent over the phone).
Also, you will find out (see the next section) that the first
guides you better in your research.
Thus, doing research requires more stamina than is typically required
in a semester-long class. With that stamina you say "OK, we
noticed this question of knowledge about knowledge; what next?"
And, you can either sit down and think, or you can ask your friends
and faculty, or you can search the WWW. One of those (after you
did not get persuaded to do other things) would point at Modal
Logics and some books on reasoning about knowledge. You read
those, and start working on a formal system that can represent
knowledge about knowledge, when each of the sides (knowledge) is
Remmeber, you are never in a vacuum, even when you think that you came
up with a question that is so different that there's nothing relevant
to it in the literature.
An Algorithm for Good Research Papers
What I usually do is
All of this process normally takes around half a year (normally
distributed around that 1/2 year mean).
start working on the question,
- develop it in the direction I think it should go, namely, I
play with the question and form the answer the way I think it
should be in guidelines.
- Then, I have a better understanding of the problem
- I go and search for topics that could mention facets of my
- Normally, I find something that is not too close but gives me a
thread of literature to follow for a while.
- Then, I go and revise what I have done, and progress is made
much farther than before.
- Then, I again go back and look for more relevant
topics. Normally, at this stage (third iteration of going to
literature) I find things that are really close, so
close it is a little scary at first - was I scooped 3 years
- Then, normally, I look closer and see that they really did
something slightly different, and that my results have better
performance in some ways, and that also I can answer questions
that the previous guys did not. I summarize these differences.
NOTE: Many researchers run out of steam
at this point, and just are satisfied with their little advance.
This is where most peope are when a conference paper is due,
and they have to decide if their progress is good enough.
- At that point (depending on how better my work is and how
different) I usually revise the work completely and from a
different perspective. Here comes the importance in
choosing a question that is good enough from a scientific
perspective. Just ask yourself what is the next step
after this work is complete. If your competitors did a
good job in ansewring the question, then your in an even
better position than before because you can now build on
their work. If they did not do such a good job, then it is
your challenge to do the work such that others (and you) can
build on it. Build what? Whatever you had in mind that helped
you choose the research question in the first place (see the
previous section on choosing a research question).
- At this point you have gained enough insight into the technical
problem that you can see and come up with much more mature
results, and rewrite your work in a form that is close to
the final version. Perhaps one more iteration of "find related
work", "explain my findings and my question clearly", and
"motivate by telling people the greater story". Remember, you
are writing this paper for people other than yourself.
This is enough of the story for now. I think it gives you some
perspective on why it is hard to make much progress quickly and
without initial guidance . You see, it is like writing a real software
application. It is not something you do in a day or even a month,
unless it is very simple. Think about creating a Doom-style game from
scratch by yourself (not using any software packages created by others).