Getting Your Research Program Started

Seminar notes from a talk given on September 22, 1993

by David Whalley & John DeCatrel at Florida State University

1.  How does one identify a faculty member to work with?

1. Talk to faculty members.  Find out what they are currently working on and if you are interested.  They may (or may not) want to work with you.  See what sort of research funding is available. 

2. Talk to current or former students.  Are the demands placed by the faculty member one that you would enjoy or, at least, be able to handle?  On a personal level, will you be able to work with, and take instructions from, this person?

3. You may want to make inquires at other institutions, especially at the PhD level.

2.  How does one get started in research?

1. Assume that you have identified an area that you and your prospective advisor will work in.  Your advisor may have a specific reading list and funded/unfunded project.

2. Take any prerequisite courses, then advanced courses in the area offered especially, but not necessarily limited to, the advisor.

3. There may be tutorial books or collections of papers in the area published by, e.g., ACM, IEEE, Morgan-Kaufmann.

4. There probably are collections of classic papers, and some classic books that you should read.  These are generally not state of the art, but are invaluable in giving you a solid foundation. 

5. Read current papers in conferences and journals in your new field.  Attend a conference or two if feasible.

3.  How does one come up with an idea?

1. Keep current.  Know what is going on in your areas of interest.  It isn’t useful to come up with an idea that has already been investigated.

2. Don’t always accept what you read.  The author will write a paper to make it look good.  If there are quantitative measurements, then check the details (input data, test programs, etc.).  Often the conclusions may be drawn incorrectly at the end of a paper (based on opinion rather than empirical evidence).

3. Look at the future work section of papers.  Often the authors have no intention of following up on these ideas.  If they do, then they often say they are currently working on it.

4. Attend conferences and discuss ideas with peers.  Attend the panel discussions at conferences.

5. Try to keep your own research projects current, even if you don’t see any immediate publications from it.  Ideas for papers are often generated by encountering difficulties and overcoming these problems.

4.  What is “too large” or “too small” of a topic?

1. Most likely the topics you examine to write a thesis will be too large.  A broad problem is usually very difficult to solve.  The problem may have already been partitioned and its pieces researched by dozens of people.  One of these pieces may be suitably narrow, and have some remaining open questions that you can work on.

2. Look at other people’s theses and get a feel for the scope of their problems addressed.  Of course, it’s better to examine “good” theses.  There are plenty of poor ones out there.  Obviously theses in your area, perhaps available via inter-library loan, serve as better references than those outside of your area.

3. The chances that your thesis will solve some fundamental, outstanding problem in your discipline are minuscule.  It’s better to focus on a problem not overly challenging, but terminable within a year.  That doesn’t mean that your problem has to be uninteresting.  Do resist the urge to develop your own scientific area.  Incremental improvement over problems already identified is safer.

5.  How do you pursue your idea?

1. Set up an environment to do research.  A good environment will allow a researcher to concentrate on the new idea rather than the mechanics of setting up the experiment.  Ideas can be obtained when setting up tools and environments.  Descriptions of tools and environments can also be sources of papers.

2. Start working on an idea.  You don’t have to be totally sure of it before you pursue it.  If one were sure, then it wouldn’t be research.  By pursuing the idea, one can often come up with several other new ideas.  Having a nice environment for experiments will encourage one to start the research.

3. Analyze the idea thoroughly.  Pretend you are the reviewer of the paper and think of criticisms.  Try to address these criticisms (fill all the holes you can).  It is much better to thoroughly research a simple idea with limited applications, than poorly research an idea with much greater possible benefits.

4. One has to also understand the idea of diminishing returns.  You can’t evaluate a topic forever.  If some additional analysis will produce very limited benefits, then don’t do it.

5. Look for ideas that can be quantitatively evaluated.  I am not saying that qualitative subjects are not interesting or worthwhile.  Unfortunately, evaluation of qualitative topics is just more difficult to sell to editors, program committees, and reviewers.