#19 from R&D Innovator Volume 2, Number 1 January 1993
and Scientific Progress
Yalow won the Nobel Prize in Physiology or Medicine for developing
an assay for extremely small quantities of material in biological
fluids. She is senior
medical investigator at the Veterans Administration Medical
Center, Bronx, New York.
miracles of science do not arise from the many, but from the few.
More than a century ago, Claude Bernard wrote, "Men
with a presentiment of new truths are rare in all sciences; most
men develop and follow the ideas of a few others.
Those who make discoveries are the promoters of new and
many difficult research challenges, it is impossible to predict
whether the problem has a solution, the exact experimental course
needed to achieve the solution, the timetable for its completion,
and whether an unexpected finding will divert the effort toward a
new direction. This
uncertainty produces an inherent conflict between a review by
peers and the ability to pursue a pathbreaking research strategy.
me give an example from my own career.
Our initial report demonstrating that therapy with animal
insulins caused an antibody response was rejected by a major
journal. Although it
was eventually accepted by another journal, that was only after we
were forced to retract our major conclusion --that the protein we
found was a real antibody. The
problem was that, under the scientific dogma of that time,
proteins as small as insulin could not induce antibody formation.
that dogma has been supplanted by a more accurate version of
reality, allowing me the satisfaction of inserting the rejection
letters in my Nobel speech.
I had then been forced to depend on today's system of basic
research grants for funding, I doubt this vital discovery would
have occurred. Remember,
I learned from reviewers and editors at two leading scientific
journals that my conclusion was outside conventional wisdom, and
therefore scientifically impossible.
researchers must not only submit to before-the-fact appraisal by
peers; they also must present detailed work plans stretching far
into the future. What
problems do such plans cause?
the mind-set required to predict the path of research puts
"blinders" on an investigator and clouds the recognition
of vital but unanticipated findings. Thus, potentially valuable ideas may be seen as inconvenient
and unnecessary diversions to meeting the plan.
if academic or industrial researchers are rewarded for hewing to
the original line of research, they have less incentive to pursue
novel advances. Thus,
interesting ideas or observations that could lead to new concepts,
processes, or measurements—that may have been discovered—are
"magically" converted to lost opportunities.
plans do have a function—to direct research and allow the
funding sources to achieve their priorities.
But, in light of the drawbacks mentioned above, how can we
supplant detailed plans and still keep some control of research
suggest evaluating established investigators with retrospective
review rather than prospective planning.
This review would focus attention on a detailed analysis of
the investigator's record. Someone who already has made an above-average number of
contributions is likely to be more valuable than someone who just
completes projects according to plan—someone who "meets the
quota." In the
long run, the former person is more likely to give the company or
department a competitive advantage.
the academic community, grant requests, perhaps submitted at
three-year intervals, should demonstrate that the investigator has
used existing funds effectively.
If evidence shows increased or decreased productivity,
funding would be altered accordingly.
obvious question becomes, how can new investigators enter the
system? I would
assess new people on their early accomplishments and supervisor's
suggestion clearly places heavy responsibility on supervisors to
give subordinates a chance to grow, identify people with a true
flair for discovery, and to divert the others to paths where such
skills are less likely to be needed.
Clearly, a supervisor cannot do this without day-to-day
interactions with the staff.
Although too many supervisors have neither the time nor the
interest for such involvement, it should receive high priority.
troubled that many researchers are becoming less productive
because they divert their skills away from the goals of producing
quality science and technology.
Too many people in the scientific community now are driven
by motives aside from the desire to make practical or basic
discoveries. The accoutrements of success—large laboratories,
significant funding, travel to many meetings at home and
abroad—have overshadowed the joy of discovery.
And too many scientists feel tempted to cut corners due to
competitive pressures and the rapid pace of contemporary science.
Science advances most productively when we focus on
scientific merit rather than on the potential for attracting fame
or increased funding.
years ago, Leo Szilard wrote in Voice
of the Dolphins and Other Stories that research progress could
be stalemated if researchers were forced to commit all their time
to writing, reviewing, and supervising funding.
His baleful description eerily anticipated today's
situation in U.S. academic science.
And it's perilously close to what's found in industry.
seems that a continually increasing percentage of our budget and
energy goes into the review process—both reviewing others and
preparing for review of our own work.
How effective are these reviews?
Is it heretical to suggest that the pace of real advances
might be quickened with less funding if research is managed with