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[交流] [原创]small science is good science美国科学院主席如何看待科学

美国科学院主席Bruce M. Alberts去年在复旦大学做讲座时提到一个观点，small science is good science（biology领域），并提到他曾经为此在cell上发过一篇文章。我现在为big science所困扰，把他的这篇文章找来。我发现，他在文章中所提到的大实验室可能会出现的问题，我所在的实验室几乎没有一条没有的。我把此文贴在这里，希望能对准备考研和考博的虫子有所启发。
imits to Growth: In Biology,Small Science Is Good Science

These days, many people grow up believing that bigger
is better. Giant factories that produce Wonder Bread have
replaced thousands of corner bakeries, driven by the increased
efficiency of scale. There is an unfortunate tendency
to extend this view to the biological research community,
and I have on occasion heard a major symposium
speaker introduced in glowing terms as the coauthor of
more than fifty papers per year. While I can admire the
energy and management skills required to maintain a very
large laboratory, the best biology is rarely done in this way.
With a few notable exceptions, the biochemists and
molecular biologists I most respect run relatively small
laboratories and publish when they have something important
to report. As I shall argue here, doing good
science is very different from producing bread, and there
are compelling reasons why large laboratories are in
general less efficient and less interesting than small ones.
To reflect this fact, I believe that changes in funding patterns
and expectations would be useful in the biological
sciences.
Several factors combine to make large research groups
inefficient. As the size of a research group increases,
more and more of its leader's time has to be spent on such
nonintellectual endeavors as helping with job applications,
finding and accounting for funds, and other organizational
matters. Less and less time is left for thinking
about science, let alone keeping up with a voluminous research
literature. In the crush of such overcommitment, I
have sometimes found myself encouraging my associates
to do obvious rather than innovative experiments, in order
to be relieved of having to spend too much of my time in
worrying about their projects. Moreover, as a laboratory
grows, one becomes less and less familiar with many of
the techniques being used-and thereby less able to
judge either their potential or their limitations.
In the worst case, a large laboratory can become a
place that simply provides equipment and supplies to
younger researchers, with very little or no research advice
or guidance. As matters now stand, most scientists who
have reached a certain level of accomplishment can find
the funds to set up such a laboratory, tf one is "lucky~' he
or she will attract enough outstanding young people into
such a group to maintain a self-sustaining level of research
productivity. Grants can sometimes even be
renewed with minimal input from the principal investigator,
being largely "ghostwritten" by younger colleagL~es.
Eventually, an NIH program project grant might be obtained,
giving more permanence to the operation. In such
cases, the group leader can become a true "science
manager"--an individual who makes very little contribution
to the actual science being done, but who spends
nearly full time arranging for funding, travelling to give
seminars and symposium talks, and processing manuscripts
from the laboratory for publication.
I believe that laboratories of the above type should be
strongly discouraged in U.S. biological science. When rewarded
with too much money, there is very little impetus to choose priorities carefully, as is required to use one's
limited intellectual resources wisely. Moreover, because of
the need to maintain the operation at a certain level of activity,
it is inevitable that most of the work being done is
rarely innovative or outstanding. Some large laboratories
tend to jump quickly to exploit the original observations of
others, believing that their extensive resources will enable
them to compete effectively.
Many large laboratories represent a poor training environment
for young scientists. Graduate students and postdoctoral
scientists are treated as though workers in a factory,
contributing strictly to their own part of the production
line. This does not prepare them to function as independent
scientists and may even impede their development
by preventing the acquisition of habits of independent research
at a crucial point in their careers. Even those rare
individuals who succeed can become disillusioned and
cynical, when they see their own ideas and efforts
credited to a group leader who made no scientific contribution
to the research that they performed.
It is also important to realize that large laboratories are
often very wasteful of resources. Per capita productivity is
important because the total number of scientists who can
be supported is limited. As an NIH study section chairman
who has reviewed numerous grants, I find it extremely difficult
to sort through computerized listings of "other grant
support" to decide whether the present grant request from
a large laboratory is really justified. Does a particular project
require five postdoctoral fellows or can it be done just
as well (or better) by three? The two major criteria that are
applied at present are those of "scientific overlap" (is the
proposed work already covered in another funded application?)
and "competency and quality" (is the investigator
able to carry out the proposed 'work and is it worthwhile?).
If the answer to the first question is "no:' and the answer
to the second question is "yes~' the grant is approvable
with a high priority regardless of the total level of other
grant support.
I believe that these two criteria are insufficient in several
respects. First, any worthwhile project is bound to produce
some unexpected results during a three to five year granting
period. Ambitious individuals who have mastered the
system will seize on each such novel result as an opportunity
for seeking a separate grant to explore all of its possible
ramifications, rather than include these studies in the
original project where they often belong. Yet there will be
no scientific overlap in the formal sense, because the unexpected
was of course not included in the original specific
aims. Most importantly, the question of competency
is crucially related to how much energy and attention can
be devoted to the new research proposal. If a proposal will
increase a laboratory's size from (say) fifteen to twenty researchers,
I contend that there is a strong likelihood that
the project will not receive the type of attention from the
principal investigator that is required to make it outstanding,
regardless of the quality of the application.
There is a rational way of dealing with these problems.I suggest that the NIH (and other agencies) set a formal
ceiling on the total amount of funding from all sources (including
private foundations, program project grant allocations,
etc.) that may be used to support the laboratory of
any individual principal investigator. The limit should reflect
the amount of research with which one investigator
could be closely involved on a day to day basis. With current
costs, one might envisage a limit in the region of
$300,000 to $400,000 per year. Although funding above
this level could still be possible, it would require evidence
of some very exceptional merit or need--for example, a requirement
for especially expensive reagents or animals.
Such a plan would of course save funds and thereby allow
more scientists to be funded. By setting a limit to the
size of the laboratories that most of us could hope to run,
it would force each of us to spend more time on science
and less on grant writing, local negotiations for more laboratory
space, and other aspects of scientific administration.
The net result would be a better general research environment,
as well as more opportunities for independent
work by young scientists.It is crucial to recognize that many important research
results start as surprises whose implications can easily be
missed, and that money is no substitute for careful observation,
thoughtful analysis, and scientific skill. Moreover,
a single innovative and original publication is worth much
more than ten obvious ones. One could argue that the
surest way to destroy a young scientist would be to give
him or her eight technical assistants in constant need of
supervision and advice, and the motivation to work on
three different projects at once. Science is not a business
and bigger is not better. What we want to encourage from
the best young people is perhaps one paper per yearone
that makes a real contribution and will be worth reading
even years after its publication date. Any value system
based on acquiring the largest research team, or on maximizing
either total grant support or publications, is counterproductive
to good science and should be viewed with
alarm.
Bruce M. Alberts

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