Kahn, C.R. Picking a research problem. The critical decision. N Engl J Med 330, 1530–1533 (1994).

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There is probably no question that plagues investigators, especially young investigators, more than how to pick a research project. This decision is not one that must be faced only once in a lifetime; rather, it must be continually revisited. Although it is easy to assume that success in research is just the difference between good and bad luck (and indeed there is a certain amount of luck in research), most highly regarded investigators will have many successful research experiences during their careers.

For the new investigator and junior faculty member just starting his or her career, the decision about a research project is further complicated by many other questions. How should one weigh high-risk, high-interest projects against lower-risk projects of lower interest? How similar or different should the project be from work done during one's postdoctoral fellowship? Can one remain in the same institution as one's postdoctoral mentor and still make an impact, and if so, how is this best achieved? How many different projects should an investigator attempt to be involved in or undertake? How important is complete independence? When is collaboration good, and with whom? Should the M.D. investigator do anything differently from the Ph.D. investigator in picking a research project? What do you do when you are faced with some aspect of a project for which you are not technically prepared? How should one balance projects funded by the National Institutes of Health (NIH) against projects without such funding? In contrast to the rich scientific base that underlies the research itself, little has been written to help the investigator facing these challenges1-6. Clearly the answers to these questions depend on the exact circumstances, background, expertise, and desires of the individual investigator, but every investigator should have a strategy for picking a research problem that optimizes the chances of success.

The first step in picking a research project is to understand what makes research “good.” Indeed, considering the extremely competitive nature of research funding and the rigorous review process used by top academic institutions for promotion, this question should be more accurately phrased, “What makes a research project outstanding?” Certainly, there are fundamental characteristics that everyone would agree are important. The study should be well performed and use appropriate and up-to-date forms of technology. The data should be carefully analyzed and accurately reported. For studies involving animals and humans, ethical considerations must be dealt with appropriately. But is this enough? Are these the variables that make us feel that the work of one investigator is superior to the work of another? Usually not.

In my opinion, there are several features that make a research project “outstanding.” First, it must ask important questions. If the question is not important, then it is likely that no matter how carefully the study is performed, how accurately the results are tabulated, or how well the work is reported, this will not be viewed as an outstanding piece of work. Second, if possible, the project should have the potential to yield a “seminal” observation -- one that creates truly new knowledge, leads to new ways of thinking, and lays the foundation for further research in the field. We often recognize a seminal observation as the first major publication in an area, which sets the stage for subsequent work and will be followed by many reports from the same and other laboratories extending and developing the point and expanding it to related areas. If these first two criteria are met, the remaining criteria for good research are usually easily fulfilled. Thus, the results of the project will be publishable in respected journals, recognized and cited by peers, presentable at high-quality meetings in the field, and of course, fundable on competitive grant review.

It is important to recognize, however, that frequently, at the earliest stages, work leading to a seminal observation goes counter to existing dogma. Thus, peers may be skeptical, making it difficult to publish the work in the “best” journals and difficult to obtain competitive grants. Over the past several years, very tight NIH funding has made this problem much worse and no doubt has led to a loss of creativity in science, as more and more investigators attempt to ride the trends in science rather than seek new avenues for investigation1-3. In such cases, the wise investigator must determine, by discussion with trusted colleagues, whether the work has the potential for real importance, find the capacity to stick with the project, and fight to obtain financial support until the rest of the scientific community recognizes its value.

With these points in mind, picking a research project can be viewed as a series of discrete steps or thought processes that might be termed the “Ten Commandments for Picking a Research Project.”