Back to May 2006 CRN Table
[Published originally in the May 2006 edition
of Computing Research News, Vol. 18/No. 3]
Are Computer Scientists Timid?
By Peter A. Freeman, Assistant
Director of NSF for CISE
But, we’ve become too timid in many of the ambitions we collectively
and individually have for our field.
I start to come to that conclusion when I hear from our Program
Directors that too few of the proposals they see offer truly innovative
ideas that excite panels or themselves. While confirmatory or
incremental work is essential, we must also have a continuous flow of
exciting, innovative ideas (and the community must ensure they are well
received, and then we must ensure they are funded).
I am even more convinced that we need to regain the excitement that
brought many of us to the field when I hear the incessant—but
clearly important in the near term —discussion of why CS
enrollments are falling, focusing on whether there is too much math
required (probably not, IMHO) or whether we need a big ad campaign
(probably, but to advertise what?) or worse, whining about why field X
is getting more funding than field Y (both within CS and in comparing
us to other fields).
I definitely conclude that we need to regain our grand aspirations when
I review the entire NSF portfolio in detail each year and see the deep
and often grand quests of other fields—quests with no discernible
practical result that may take decades of dedicated and fundamental
work, involving theoretical work that will break entirely new ground,
or requiring grand experimental projects that may total billions of
I absolutely know that there is something fundamentally different about
the tenor of much research today when I think about the visions of even
a few of the giants of our field like Doug Engelbart, Alan Kay, Herbert
Simon, Carver Mead, Gordon Bell, or Juris Hartmanis—just to name
a few from among a good many more that had (and still do!) truly grand
and audacious ideas.
Where are the
BHAGs (Big Hairy Audacious Goals) of today?
As we are developing the Computing Community Consortium  and as I
talk with many computer scientists at all levels, the question of the
vitality of our field springs out. That question should concern
every one of us, most especially those of us in positions of
leadership. It is a question for which there are multiple answers and
multiple rejoinders—all of which deserve to be heard and explored.
Let me comment briefly on the current national focus on
“innovation.” I believe all of you would agree that
it is a long-overdue and very important step. Whatever
disagreements one might have with the American Competitiveness
Initiative (ACI)  I hope that you will join me in applauding,
supporting, and strengthening it.
Computer science and the applications it has spawned can rightly claim
to have been the engine of much of the innovation that has been driving
the U.S. economy in recent years. While the “irrational
exuberance” of the late 1990s led to the crash of many ventures,
the underlying theme of innovation in the IT industry—and those
industries whose operations are now enabled or enhanced by IT
products—has continued more or less unabated. Likewise, utilizing
CS as a peer in a number of research activities is leading to
fundamental innovations throughout science and engineering.
Doesn’t this demonstrate the vitality of our field? Doesn’t
this deny my assertion that we may be too timid in our goals? At one
level it does—until you ask what fundamental concepts and
research these innovations depend on when you trace back their
More to the point,
where are the fundamental changes in computer science?
If you ask that question, then I believe that you will agree with those
who are now successfully pushing for more fundamental research in
science in general.  The basic message is that we are in danger of
losing the kind of edge we have in end-result innovation in this
country because we are not asking deep enough questions and pursuing
We need to explore entirely new concepts and we need to do that in new
ways, whether in theoretical and small-scale research or large-scale
experimental projects. Fundamental results typically start in
relatively small, even individual, efforts. We must not forget that,
but just because a project is small-scale doesn’t mean that it
will result in entirely new concepts. As an example, the Science of
Design effort  is intended to break us out of a box regarding how to
At the same time, it is essential to employ experimentation wherever
possible to enable the kind of future usage of CS concepts that the
world is madly rushing toward, but won’t be able to reach solely
with today’s stock of fundamental ideas. Further, experimentation
need not be limited to the systems builders. If you draw parallels to
physics—where huge experiments are carried out to validate a
theory—or astronomy— where observations lead to
theorizing—and note that in both cases there is then a
“virtuous cycle” between the two modalities, then I hope
you see the opportunity for computer science. Indeed, some already
A new modality of experimental research in a number of CS fields may be
possible, and it may require substantial instrumentation (in NSF lingo)
to carry out. We should not be timid in conceiving of, planning for,
and requesting such research infrastructure, just as other sciences
routinely do. The Computing Community Consortium described elsewhere in
this issue is expected to do exactly that over time for all areas of
An example of this kind of instrumentation is the Global Environment
for Networking Innovations (GENI) initiative. It is an instrument for
use by CS researchers in doing their fundamental, experimental
research. This demands that it be open and accessible for measurement
and for ad hoc changes at all levels and in all aspects. We are
currently seeking community input to make sure that this is the case.
This is essential to experimentation, and is a fundamental requirement
that we are placing on the design.
Another way to look at such instrumentation-intensive projects is as
prototypes for future practical and operational IT-based artifacts. We
have ample precedents in our field in which research artifacts
ultimately turn into products that turn the world upside down. Do you
remember what SUN stands for, or know where Google developed, or
understand the role that TheoryNet/CSnet/NSFnet played in creating
But, our primary
objective should remain to push forward our scientific understanding of
computation and the devices/systems that instantiate our theories.
While that may happen in the case of an infrastructure-intensive
project—and then again, may not—it often begs an important
set of questions from those who pay for research along the lines of:
“How are you going to transition results into the practical
world?” There are two answers to that question: one short term
and one deeper, but both important.
The short-term answer is that as important as “technology
transfer” is, our mission is to advance fundamental research.
Given that there are any number of fundamental things we don’t
understand about the structure and operation of complex IT systems, we
believe that attempting to develop such an understanding is valuable in
its own right. Just as other fundamental scientific questions engage
legions of people and tons of money for decades, we believe these
questions stand on their own as worthy of investigation.
Nonetheless, as a practical matter, we must pay close attention to the
issue of how we can enhance the ultimate transfer of results into more
practical results. Our field and the industries it has spawned have a
rather good record, in fact, of rapidly making money and improving
lives with ideas and theories and prototypes that were in the lab or
being talked about at academic meetings only a few years ago—the
examples are abundant.
The deeper answer is one that is important to understand as we
collectively try to advance our field. Computer science is not science,
not engineering, not math—but a combination of all three. That is
hardly an original observation, but the rub is that because we are a
new field (yes, new even though some of us have been in the field
almost half a century) we are still working out just what that answer
means in terms of what we do as researchers and educators. Do some of
us belong to just one of those fields, but still call ourselves
computer scientists? Do we do math or science at one phase of research
and engineering at another? Do we do something that is somehow a bit of
all three and we just can’t describe how that works? Did we
originate in one field and are moving toward another?
When I think about the vitality of our field, I’m less interested
in an abstract answer to these questions than I am in helping determine
what we should be doing. In that context, I believe we have lost some
of the original vision and vitality of the founders of our field who
were not afraid to ask big and deep questions, and to experiment where
appropriate to find the answers to their questions. To some extent I
think we have lost our way as scientists and let the inner engineer
(and entrepreneur!) in each of us become too ascendant.
The questions our field truly faces are not questions of why students
don’t love us or why decision makers don’t give us enough
money—they are the exciting, compelling questions of
understanding some of the most complex artifacts ever created (or
discovered, for that matter) and of attempting to create new theories,
understandings, and artifacts that far transcend anything we have today.
As a professor, dean, and now research funder, I well understand many
of the factors that push us toward the safe, rather than the
innovative, path in research and education. If there was ever a time to
overcome and ignore those factors—at all levels—it is now.
We all have an important role: Those of us at funding agencies and
research labs must set higher expectations and educate our colleagues
on the importance of our research and education; academic and lab
administrators must reward true advances, not just incrementalism; and,
most importantly, each researcher and educator must continually strive
to contribute to the advance of our field in fundamental ways.
Don’t be timid!