#19 from R&D Innovator Volume 2, Number 1          January 1993

Review and Scientific Progress
by Rosalyn S. Yalow, Ph.D.

Dr. 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.

The 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 fruitful ideas." 

In 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.

Antibodies?

Let 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.

Fortunately, 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.

If 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.

Too Much Planning?

Today's 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?

First, 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.

Second, 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.

Research 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 funding?

I 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.

In 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.

Frequent Interactions

The obvious question becomes, how can new investigators enter the system?  I would assess new people on their early accomplishments and supervisor's recommendations.  This 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.

I'm 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.

Thirty 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. 

It 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 greater perspicacity?