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1. A Case for Strategic Research
Peter EisenbergerJames S. Langer
Citation: Physics Today 48, 4, 78 (1995); doi: 10.1063/1.2807979
View online: http://dx.doi.org/10.1063/1.2807979
View Table of Contents: http://physicstoday.scitation.org/toc/pto/48/4
Published by the American Institute of Physics

2. OPINION
A Case for Strategic Research
Peter Eisenberger and James S. Langer
A call for "strategic research" was
central to the recent struggle
within the US Senate, the Clinton Ad-
ministration and the National Science
Foundation over the direction of the
American research enterprise. No-
where to be heard has there been a
constructive response by US physi-
cists to the real issues at the core of
that debate. Most of the voices that
we do hear argue for a return to the
glories of the past. We believe that a
much more realistic and forward-look-
ing response is in order.
These ought to be very good times
for physicists. We ought to be feeling
like kids in a candy shop, our main
difficulties being how to choose re-
search topics from among the great
wealth of intellectual opportunities
that have opened up in recent years.
Cosmology and astrophysics; atomic,
molecular and optical physics; con-
densed matter physics and materials
science all are enjoying an abundance
of conceptually challenging, new dis-
coveries. Supersymmetry in particle
physics is alive and well. Our recent
glimpses into the physics of biological
systems show us just a tiny corner of
a vast new world of scientific inquiry.
In this situation, the term "strate-
gic" should have an entirely positive
meaning for us; there is no reason for
it to have become a catchword symbol-
izing retreat from "pure" or "curiosity
driven" research. Acting "strategi-
cally" should mean simply that more
of us are working on projects that are
interesting not just to ourselves but
also to others, particularly those in ar-
eas outside our own specialties. In
short, it should mean maximizing our
impact on the world around us.
Isn't this what we have been doing
all along? For the most part, prob-
ably so. But maximizing our impact
PETER EISENBERGER IS the director of the
Princeton Materials Institute at Princeton
University. JAMES LANGER is the director
of the Institute for Theoretical Physics at the
University of California, Santa Barbara.
has been relatively easy for us until
recently. All of a sudden, the world
has undergone major changes. It has
become much more difficult for us to
respond to new challenges, while at
the same time it is becoming increas-
ingly urgent that we do so.
We are facing a political and socio-
logical crisis of unprecedented severity.
Two major elements of the crisis are
all too clear. New jobs are painfully
scarce, and the system for allocating
research grants has very nearly broken
down. As a result, many of our most
talented young physicists are abandon-
ing scientific careers, and those who re-
main in many cases are not working
on the most important and challenging
research problems.
A serious cause for concern is that
US industry has eliminated almost
all of the basic research that it once
supported and also has substantially
cut back on the development of new
technologies. This is not some short-
term lapse in judgment by industrial
managers. With the sudden decline
of defense contracts and the simulta-
neous rise in international economic
competition, risky, long-term invest-
ments in research no longer make
sense for most US companies.
In principle, this situation presents
an opportunity for US research univer-
sities. There may be sharp disagree-
ments about which research topics will
be most relevant to future sciences and
technologies, but there is little doubt
that a strong science base will be essen-
tial to the economic health and security
of the country. If responsibility for
maintaining this science base is no
longer to be shared by industrial labo-
ratories, then academic scientists may
have larger roles to play. Pressures
on the research universities, how-
ever, are moving them in exactly
the opposite direction.
For about half a century, by far
the most important contribution of
US universities to the nation's tech-
nological capabilities has been the
steady stream of young scientists and
engineers who have moved into indus-
try, government laboratories or myr-
iad other occupations for which they
were qualified by virtue of their aca-
demic experiences. In moving from
the universities to industry—and
often back again—these graduates
have provided the most effective of
all mechanisms for the transfer of
knowledge and technology.
In physics, a few PhDs tradition-
ally have found permanent employ-
ment within the universities, but the
largest numbers of graduates have ap-
plied their versatility and problem-
solving skills to a wide variety of non-
academic careers. In the last few
years, however, these professional op-
portunities have all but vanished. If
this system is no longer to be opera-
tive—if the national effort in basic re-
search no longer requires new scien-
tists and engineers—then the research
universities are indeed facing a pro-
found challenge.
Critics of the universities have sug-
gested that research faculty could diver-
sify their interests and shift their priori-
ties away from what the critics perceive
as unnecessarily narrow and esoteric re-
search. The first answer to this criti-
cism, of course, is that the scientific
bases for today's most important tech-
nologies seemed entirely esoteric not
very long ago. A second important an-
swer is that much of the best basic re-
search has always been inspired by
technological inquiries. It is precisely
that complex interplay between the fun-
damental and the applied that we are
struggling to preserve.
But the critics are correct in at
least one respect: We physicists have
become exceedingly conservative in
our choices of research topics. Large
numbers of investigators tend to con-
centrate their efforts in a few well-
established areas, while other topics—
often the most interesting, inter-
disciplinary or otherwise unorthodox
ones—remain relatively untouched.
For example, few physics depart-
ments have started new efforts in
biomaterials, the geosciences, pattern
formation in nonequilibrium systems,
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or the variety of new topics that some
call the "science of complexity." It is
even rarer to see programs in obvi-
ously practical but intrinsically inter-
disciplinary fields, such as materials
synthesis or instrumentation science.
To make matters worse, the barriers
between traditional academic depart-
ments accentuate the conservatism
within the disciplines.
Ironically, this trend toward disci-
plinary conservatism at a time of
broadening interdisciplinary opportu-
nities is being exacerbated by our sys-
tem of Federal support for academic
research. Competition for research
grants has become extraordinarily in-
tense, so much so that faculty mem-
bers find that the effort required for
writing proposals detracts substan-
tially from their ability to do research
or to teach effectively. The declina-
tion level for proposals is often so
high that there can be no objective
criteria for deciding who does or does
not receive funding; the peer review-
ers cannot on average be as compe-
tent as the authors of the proposals
that must be rejected.
Under these circumstances there
is a great advantage to being well
within the mainstream of an estab-
lished field, where one's work will
be evaluated by knowledgeable col-
leagues. Conversely, even the most
well-established physicist cannot write
a proposal that might be reviewed by
geoscientists, biologists, metallurgists
or polymer chemists and expect to
gain the unanimously enthusiastic
support necessary to win a research
grant. Each of us is thus strongly
motivated to find a special area of
expertise, choose relatively safe pro-
jects and pay little attention to other
possibilities.
What can be done to reverse these
trends? To begin with, the academic
physics community must be its own
agent for change; we cannot expect
the funding agencies to make changes
for us. If we believe that the rigor-
ous, analytic methods of physics are
precisely what is needed in many of
the most important emerging areas of
research, then we must take the initi-
ative to prove our point. As individ-
ual scientists, more of us must risk
exploring new fields, developing new
collaborations and even occasionally
crossing disciplinary boundaries and
treading on other people's turf. As
leaders of academic institutions, we
must recognize that all physics de-
partments need not be identical. In
the future, physicists will be playing
very different roles from those of the
past. If we do not know precisely
what those roles will be, then we
must take some risks. The funding
80 APRIL 1995 PHYSICS TODAY
agencies must follow our lead.
They too must learn to take risks,
but by their very nature, they can-
not do so unless we provide the op-
tions for them.
On a second front, we must ex-
plore vigorously and with open minds
new modes of interaction among uni-
versities, industry and government
laboratories. In doing this, we should
look at specific problem areas and try
to determine which are the crucial sci-
entific questions that need to be an-
swered. The research strategy known
as "solutions in search of problems"
will not work well for us now. We
shall need to be clear and specific
about our goals and how they relate
to the interests of others, and there-
fore we shall have to interact much
more broadly—with other scientists
and with the public—than physicists
ordinarily have in the past.
We must be careful, however, that
we do not make promises we cannot
keep and that we do not let other peo-
ple make such promises for us. In par-
ticular, we cannot let Congress measure
the success of the research universities,
and thereby determine funding levels, by
looking at their short-term contributions
to US economic competitiveness. Unfor-
tunately, that is the direction in which
we are headed, and we need to do
everything we can to counter this
trend. The legitimate measures of suc-
cess for physicists, and for the research
universities more generally, are their
contributions to the store of scientific
knowledge and their preparation of
skilled scientists and engineers. Both
measures are highly relevant to the
long-term success of the US, and we
ought somehow to be able to establish
them as the accepted criteria for deter-
mining our place in the national
scheme of priorities.
In making this argument, we should
use the term "strategic" in its most posi-
tive sense. We all know perfectly well
that many of our most fundamental ad-
vances have occurred in the process of
trying to solve practical problems. We
also know that the rate at which new
directions for research are emerging in
our field constitutes an embarrassment
of riches. Because we have the luxury
of choosing our research projects from
an extraordinarily wide range of topics
about which we are "curious," we do
not compromise our intellectual integ-
rity by "strategically" choosing to work
on those topics that are both interest-
ing and potentially useful to other peo-
ple. We'll have to diversify our efforts
and break out of our disciplinary
boundaries, and that will be good for
us. If our new versatility improves our
credibility in the larger community,
that will be all the better. •