TITLE: How to Really Succeed in Research...
AUTHOR: Eugene Wallingford
DATE: February 19, 2007 11:39 PM
... when you work at a primarily undergraduate school.
My Dean sent me a link to
Guerrilla Puzzling: a Model for Research
(subscription required), a Chronicle Observer
The article describes nature as "full of intriguing puzzles
for researchers to solve". Unlike the puzzles we buy at the
store, the picture isn't known ahead of time, and the shape
and number of pieces aren't even known. Scientists have "to
find the pieces before trying to place them in the puzzle."
From this analogy, Zimmer argues that researchers at schools
devoted to undergraduates can make essential and valuable
contributions to science despite lacking the time, manpower,
and financial resources available to scientists at our great
research institutions. While some at the elite liberal arts
colleges do so by mimicking the big-school model on a smaller
scale, most do some by complementing -- not competing with
-- the efforts of major research programs.
The biggest disadvantage of doing research at an undergraduate
institution is the different time scale. An undergraduate is
in school for only four years or so, and the typical undergrad
is capable of contributing to a project for much less time,
perhaps a year or two. In computer science, where even
often requires writing code, the window of opportunity can be
especially small. My hardest adjustment in going from graduate
school researcher to faculty researcher was the speed with
which students, even master's students, moved from entering
the lab to collecting their sheepskin. Just as we felt
comfortable and productive together, the student was gone.
Zimmer points out one positive in this pace: the implicit
license to take bigger chances. When one's grad students
depend on successful projects to land and hold their future
jobs, an advisor feels some moral duty to select projects with
reasonable chances for success. An undergrad, on the other
hand, benefits just from participating in research. Thus the
advisor can take a chance on a project with higher reward/risk
How is the researcher at the primarily undergraduate institution
to succeed? Via what he calls "guerilla" puzzling:
Sometimes, small-school researchers can create a niche in their
problem space by attacking a well-defined, focused problem,
solving it, and then moving on to another. In some ways,
computer science is more amenable to this straightforward
approach. Unless you work in a "big iron" area of computing
like supercomputing, the lab equipment that one needs is
pretty simple and not beyond the financial means of anyone.
And these days one can even do very interesting projects in
parallel and distributed computing using clusters of commodity
processors. So a CS researcher at an undergrad institution
can compete on a focused problem nearly as well as someone
at a larger school. The primary advantage of the large-
school program is in numbers -- an army of grad students can
deforest a problem area pretty quickly, and it can be agile,
One thing is for certain: A scientist at a primarily undergrad
school has to think consciously about how to build a research
program, and mimicking one's Research I advisor isn't likely
the most reliable path to success.
- Start working in a new area, while the big guys are still
writing the grants they need to get started, and pick off
the easiest problems.
This strategy requires a pretty keen sense of one's field.
But it can also be helped along by listening to deep thinkers
and making connections.
One of our faculty members is collaborating on a grid computing
project with a local data center, and they are attacking a
particular set of questions that bigger schools and more
prominent industrial concerns haven't yet been able to pin
down yet. Sometimes, it's easier to be agile when you're
- Start working in an area whose solutions seem to generate
It seems to me that certain parts of the theoretical CS
world work this way. My former student's work applying
the "theory of networks" to Linux package relationships
fits into an unfolding body of work where every new application
of network ideas creates a set of questions that sustain
the next round of study. Another faculty member here has
built a productive career by following a trail of generative
questions in medical informatics and database organization
- Start working on distinctive, attractive problems.
I'm not sure I get this one. Why aren't the big guys
working on these? Presumably, they can see them as well as
the researcher at the undergrad school, and they have the
resources they need to move to dominate the problem.