The straight-jacket
of hypothesis-driven research

The advancement of biomedical research requires both leaps of discovery and the steady progress that separates one leap from another. Leaps are universally unanticipated; no one ever wrote them as specific aims in National Institutes of Health grant applications. Gradual transitions are the opposite. They are the essence of what we write as the specific aims of our grant proposals. Gradual transitions fit hand-in-glove with hypothesis-driven research.

I lament that, as presently constructed, the NIH system of funding science is locked into the straight-jacket of hypothesis-driven research. It is understandable that things have evolved in this manner. In times of tight funding, grant reviewers find it easier to evaluate hypothesis-driven research plans than blue-sky proposals. The manner in which the system has evolved has forced scientists to perform contractlike research that grant reviewers judge to be highly likely to succeed. In financially difficult times, more risky scientific endeavors with no safely charted pathway to success often get squeezed out.

We all recognize the formula and nature of hypothesis-driven research; we describe it over and over in the thousands of grant applications we write and submit for review by the NIH each year. But how should we describe the riskier blue-sky research that our granting agencies tend not to favor? I have written about this topic before, and I have suggested that this latter kind of research follows the concepts of inductive inquiry (I 2).

Central to the utility of the I 2 form of biomedical research is the definition of a phenomenon. Here is an example of a phenomenon of interest. During hibernation, the core body temperature of ground squirrels goes from 37°C down to 4 – 5°C. Perplexingly, with robust periodicity, hibernating ground squirrels warm back up to 37°C around once every 10 days. These brief periods of warming are called interbout arousals. What is the utility to the hibernating ground squirrel to periodically warm up for about a day?

To me, this is a cool phenomenon. Interbout arousals are almost perfectly periodic, and they entail profound changes in body temperature. Instincts tell me something quite important is taking place when hibernating animals warm up briefly like clockwork. As cool as this science is, it is hard to distill it down to a set of measurable, specific aims. Sure, one can say that it would be useful to do some cataloging — measuring metabolite fluctuation as a function of hibernation and entry and exit from interbout arousals. Sure, one might hope then to garner some clues that might lead the way out of the woods But it is hard to say exactly how the science would unfold in the context of the hypothesis-driven form of research we are now forced to perform. As nebulous as it might seem, my prediction is that a talented and dedicated scientist would have a good chance of making cool discoveries if offered the chance to pursue this research for the duration of a typical R01 grant from the NIH.

Were it up to me, and it is clearly not, I would demand that NIH grant applications start with the description of a unique phenomenon. When I say unique, I mean unique to the applicant. The phenomenon may have come from the prior research of the applicant. Alternatively, the phenomenon may have come from the applicant’s unique observation of nature, medicine or the expansive literature.

Phenomena abound. One of several that have intrigued me over the past decade is the speed of mouse embryonic cell duplication. Mouse ES cells divide more rapidly than any cancer cell — almost as fast as microbial organisms, such as yeast. Why do ES cells divide so rapidly, and how is hypermitotic drive facilitated? I also find it fascinating that prototrophic strains of yeast (AKA wild type, native or nondomesticated), when grown under nutrient-limiting conditions in a chemostat, enter into an incredibly robust and periodic metabolic cycle. What is the physiologic utility of this metabolic cycle, and what is the underlying regulatory logic controlling it? Finally, the vast majority of newly formed neurons born daily in the adult mouse brain die along the pathway toward differentiation and ultimate wiring into the central nervous system. Why do so many of the cells die, and by what mechanism is neuron death enacted?

I can think of hypotheses with which to begin investigation of these phenomena, but most such hypotheses would be highly biased owing to the extreme limitations of my knowledge of ES cell growth, yeast metabolism or hippocampal neurogenesis. This being the case, it would be folly to submit NIH grant applications in search of funding to support research on these topics. As mentioned above, it is not up to me to guide the NIH on how to spend its funds. On the other hand, we live in a country that is highly protective of freedom of speech. With that in mind, I happily offer the thesis outlined in this essay and close with Albert Einstein’s iconic quote: “If we knew what we are doing, it would not be called research.”

Steven McKnight Steven McKnight is president of the American Society for Biochemistry and Molecular Biology and chairman of the biochemistry department at the University of Texas-Southwestern Medical Center at Dallas.