Serendipity and ‘impact’

When I was a young faculty member at Johns Hopkins University, I served on the Ph.D. thesis committee of Suzanne Baker, a Ph.D. student in the laboratory of Bert Vogelstein, then an assistant professor in oncology. Baker’s thesis project involved trying to identify a putative tumor-suppressor gene on human chromosome 17. Based on considerable work mapping deletions in numerous human tumors, she had reduced the search space to approximately one-fourth of the chromosome. To put the finishing touch on Baker’s thesis, Vogelstein suggested that she sequence a gene that falls in the center of this region to rule out this gene as the sought-after tumor suppressor. The gene they selected was p53, the product of which had been shown to associate with a key protein from the tumor virus SV40. To everyone’s astonishment, Baker found point mutations in this gene in several tumors; they had stumbled on what turns out to be the gene that is most commonly mutated in human cancer.
 
While serendipity has been central to a number of important discoveries, the importance of serendipity can be overstated. The selection of the problem under study is also essential, as is a deep knowledge of the field in order to place incidental or unexpected findings in perspective; the great microbiologist and biochemist Louis Pasteur famously said “Dans les champs de l’observation le hasard ne favorise que les esprits prérparés” (“In the fields of observation, chance favors only the prepared mind”). Under ideal circumstances, scientific priority setting balances the benefits of exploring the unknown with its associated potential for truly novel discoveries against the selection of problems that, if substantial progress is made, will provide considerable benefit to society.

Estimating the importance of serendipity

Can we provide at least some boundaries on the balance between serendipity and problem importance? Significant discoveries can be primarily serendipitous; the result of incremental, step-by-step solving of a known, important problem; or a hybrid of the two. An example of a largely serendipitous discovery was recognized by the Nobel Prize in physiology or medicine in 2006 to Andrew Fire and Craig Mello for their discovery of “RNA interference-gene silencing by double-stranded RNA.”
 
This discovery was based on a chance observation made in the context of studies of gene regulation in C. elegans wherein a control experiment involving the simultaneous injection of both sense and anti-sense RNAs corresponding to the same gene resulted in a dramatic change in gene expression not observed for either the sense or anti-sense molecules separately. Their appreciation of this chance observation eventually revealed a widespread but largely unsuspected biochemical pathway.
 
In the same year, Roger Kornberg was awarded the Nobel Prize in chemistry “for his studies of the molecular basis of eukaryotic transcription.” This prize was primarily for the determination of the three-dimensional structure of eukaryotic RNA polymerase. This prize represents not a serendipitous discovery but rather the culmination of many years of effort by Kornberg and his co-workers on a well-recognized problem, namely the elucidation of the structure and associated mechanistic insights for a large and complex enzyme of central importance to biochemistry and molecular biology.
 
An example of a hybrid discovery is represented by the Nobel Prize to J. Michael Bishop and Harold Varmus in 1989 for their discovery “of the cellular origin of retroviral oncogenes.” These researchers were working on a fundamental problem, namely the nature of cancer-causing genes from viruses. Identifying the nature of these genes, regardless of the answer, would have been of fundamental importance. The answer turned out to be of unanticipated significance, revealing that the viral genes were related to normal cellular genes that, when mutated in some ways, can contribute to cell transformation.
 
To look at the balance between serendipity and problem selection, I examined all of the winners of the Nobel Prize in physiology or medicine and chemistry over the past 25 years and scored each winner’s contribution as either largely serendipitous, largely driven by solving a problem of known, fundamental importance or a hybrid of the two. Of the 117 Nobel laureates (as opposed to prizes, since in some cases individuals who shared a prize fell into different categories), I classified 14 as serendipitous discoveries, 72 as driven by the importance of the problem, and 31 as hybrids. This classification is, of course, somewhat subjective. Furthermore, the choice of Nobel laureates for analysis clearly represents a highly selected group. With these caveats, the analysis reveals that serendipity was the primary driver in approximately 10 percent of these accomplishments and a substantial contributor to an additional 25 percent.

Judging potential impact

The balance between selection of important problems and the potential for unanticipated discoveries has been the topic of much discussion. Marc Kirschner of Harvard Medical School recently published an editorial in Science magazine titled “A Perverted View of ‘Impact,’” in which he criticizes the use of “impact” and “significance” as criteria in peer review by the National Institutes of Health. I agree with Kirschner that the use of these terms has the potential to distort judgments about the potential consequences of supporting specific proposals. However, as someone who was involved in the NIH Enhancing Peer Review project that led to the incorporation of these terms, I can provide some context.
 
First, what concerns about peer review led to the incorporation of these terms? Much of the discussion with stakeholders both inside and outside of the NIH focused on the fact that grant-application reviews often were preoccupied with the fine details of the scientific approach rather than the proposed problem. Many indicated that they felt the potential importance of the problem was receiving too little attention.
 
Second, the choice of the term “impact” was not intended to mean short-term influence on human health but rather the potential for changing the landscape of the research fields involved, regardless of whether these changes were close to a human health or clinical setting or were fundamental changes in our understanding of basic biology. Unfortunately, this broad perspective on potential impact sometimes has been lost during implementation, to some degree within the NIH but, in my opinion, to a greater degree by reviewers who interpret impact to mean translational impact.
 
This misinterpretation of impact may be driving research toward the middle of the clinical-fundamental continuum – that is, away from fundamental studies toward translational ones, even if these are quite far removed from true clinical applications.
 
This middle region may, in fact, be the least fertile area for real progress. Fundamental research often turns out to be most influential when it is addressing basic biological processes of which our understanding is incomplete (i.e., most processes), and important discoveries often are made in model systems that are most amenable to controlled, detailed study without regard to direct clinical translation. In contrast, research at the clinical end of the continuum often is most effective when a very well-defined clinical context is provided for the proposed study.
 
History has shown that many of the important applications of fundamental knowledge could not have been anticipated, and pushing applicants to propose such applications can distort the basic research. Indeed, the National Institute of Neurological Diseases and Stroke recently reported a detailed analysis that supported the notion that applicants are moving away from truly fundamental research to the detriment of the long-term mission of the institute.

A balanced framework

One of my former colleagues at the NIH (now retired) described to me very succinctly what he felt he needed to make rational funding recommendations. He proposed three questions (which I have modified slightly):

  1. 1. How important (either fundamentally or in terms of applications) is the project if it is successful?
  2. 2. What are the chances that the project will be successful (in the hands of the investigators involved)?
  3. 3. What are the chances that something unanticipated will be discovered along the way?

These questions capture the need to work on something important (with importance defined in a context-dependent manner) and an integrated view of the approach and the skills and previous accomplishments of the investigator(s) while acknowledging the potential for serendipitous discovery. I have found this to be a useful framework for guiding my own research planning, and I hope you may as well.

Jeremy BergJeremy Berg (jberg@pitt.edu) is the associate senior vice-chancellor for science strategy and planning in the health sciences and a professor in the computational and systems biology department at the University of Pittsburgh.

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