A single day in the life of a clinician presents innumerable problems worthy of investigation. An example: Vascular insufficiency of the lower extremities is a devastating condition commonly diagnosed in diabetic patients, smokers, and the elderly. It's a single disease, yet it offers many problems that a researcher might address. How can the condition be prevented? Could an existing mechanical aid such as an elastic support stocking be improved? If amputation is required, what wound-healing issues will arise? Could stem cell injection into the affected leg offer therapeutic benefit?
Which of these--or other--problems a researcher chooses, and how those problems are defined and pursued, determines the course of a scientific career. Choose a problem that's especially rich and you'll be doing important work for decades. Choose a problem of limited scope and you've limited the scope of your research career.
This article was developed in collaboration with the American Federation for Medical Research  (AFMR).
So, how do you choose well? Great problem finders are able to make conceptual leaps, applying solutions and techniques from other disciplines to problems of their own. But even people who aren't predisposed to such intuitive, creative leaps can achieve similar results by taking steps to approach problems--or solutions--with a multidisciplinary mind.
Psychologists Jacob W. Getzels and Mihaly Csikszentmihalyi have studied problem finding--"the way problems are envisaged, posed, formulated, created,"  in their words--as a key component of achievement. Whether working in art, business, or clinical investigation, great problem finders can look at the same phenomena that others have observed--sometimes for centuries--and perceive gaps of understanding and offer new perspectives that lead to a creative solution.
Getzels and Csikszentmihalyi identified psychological attributes of artists who were particularly creative problem finders: This group typically demonstrated a willingness to switch direction when new approaches suggested themselves. They were open to reformulating problems as they experimented with different perspectives. They were slow to judge their work as absolutely finished, and they were able to evaluate critically the probability that improvements were achievable. Artists who rated high in these areas were judged to be exceptionally creative, and follow-up studies of their work 18 years later demonstrated that they achieved a higher degree of professional success than did their less creative colleagues .
Another study, this one of artists and scientists, compared those who were critically acclaimed with others who were professionally merely competent. This study found that the former spent more time and energy on problem finding .
Broadly, scientific investigation may start in two ways, either of which may be fruitful. A "problem focused" approach begins with a question that stimulates studies to look for answers. Sometimes, however, new solutions to a specific problem appear that suggest potential application to other problems. Examples include stem cell injection for lower limb vascular insufficiency, gamma-knife irradiation for obsessive-compulsive disorder, endoscopy for brain tumor resection, and deep-brain stimulation for depression. Repurposing solutions for new clinical problems requires a multidisciplinary mind; that is, scientific curiosity about other disciplines and the time to learn about progress in specialties outside of one's own.
A clinical, contemporary example of a multidisciplinary mind is Judah Folkman, the pioneer of angiogenesis research. Even as a student, Folkman was innovative: He developed a new technique for hepatectomy for liver cancer and the first atrioventricular implantable pacemaker. Later, he and a colleague reported the use of implantable polymers for the sustained release of drugs, which allowed the development of Norplant. In 1971, Folkman proposed that all tumor growth is angiogenesis-dependent, a theory that was originally met with ridicule and disbelief among his surgical colleagues. Before his death, Folkman began to explore treatments with angiogenesis inhibitors for conditions as seemingly disparate as myocardial infarction, diabetes, macular degeneration, and even obesity .
If Folkman is a prototype of the multidisciplinary, problem-finding mind, his example suggests the personality traits that promote creative clinical investigation: curiosity and exposure to areas of medicine outside his own specialty, radical thinking, an ability to take a risk, the capacity to persevere despite ridicule and failure, exceptionally high energy, and the ability to inspire and collaborate with colleagues. Until the end of his life, he evidently was willing, if not eager, to remain on the steep part of the learning curve, reaching out to areas far outside of his core discipline.
The challenge of problem finding is that scientific discovery usually develops in slow, incremental steps, not leaps--and in clinical medicine, the process is especially slow. National Institutes of Health funding, the gold standard of research achievement, rewards proposals based on small, forward additions to a carefully constructed base of scientific achievement. Academic promotion rewards those who develop deep focus in a narrow niche.
Likewise, academic medicine has traditionally existed within well-demarcated specialties. Specialty boards and academic societies further isolate specialists, and generalists are often not highly valued. Although these silos allow specialists to achieve great experience with specific clinical conditions, they may also limit our ability to progress in leaps. The current movement toward multidisciplinary centers of clinical care and support for translational research is critically important to speed the process of discovery.
Yet, to an extent, it shouldn't matter if the labs are on the same floor as the hospital ward. The critical moment occurs when a clinician can think across disciplines about how a cellular process may be active in many different diseases, as Folkman did. Further, that conceptual marriage is meaningless unless the thinker is able to see and appreciate the significance of the problem. To achieve proof of concept requires emotional and professional investment in the idea, institutional or collegial support, funding, commitment of time and energy, and the willingness to tolerate the risk of failure.
Although some minds seem more innately predisposed to creative, multidimensional thinking, there are ways to stimulate a problem-finding, multidisciplinary mind:
Exposure to unusual stimuli: A truly unique, original idea is very rare and may not even be necessary for creative productivity. Instead, creativity is often a matter of exposure to new stimuli and repurposing ideas and techniques already used in another field. To do this, the clinical investigator should talk to colleagues, read journals or listen to podcasts, attend meetings, and watch for new developments and ideas in other disciplines.
Listen to silence and observe the 'negative space': Artists speak of the negative artistic space created by the positive images painted on a surface. Psychiatrists listen for what is not being said in therapy as a clue to repressed material. Part of the process of human acculturation is an unconscious collusion to remain blind to the most obviously observable phenomenon, if it lies outside the realm of how we always do things. Yet the seeds of innovation and progress often lie within the domain of that which is ignored or even denied. For instance, specific clinical interventions are often developed for a single demographic group, defined by gender, race, or age. Interesting scientific questions arise from considering the intervention for other groups. As an example, HPV vaccination is currently recommended only for girls, but epidemiologists and clinicians are beginning to comment on the consequences of allowing males to function as an unchecked reservoir of the virus.
Recognize the problem after the answer has been found: The history of the discovery of penicillin is a fascinating example of a solution that was discovered over and over again for many centuries before its importance was appreciated. For more than 1500 years, observations had been made about the ability of fungi to inhibit the growth of bacteria . Reportedly, Arabian stable boys stored their saddles in damp, moldy areas because the moldy saddles prevented the development of saddle sores. In 1852, J. R. Mosse published a report on the use of yeast to treat infection, followed by Joseph Lister's unpublished observation in 1871 on the ability of Penicillium glaucum to inhibit bacterial growth. In 1897, French medical student Ernest Duchesne published the results of an elegant series of experiments; however, he did not publish further and his discovery lay neglected for decades thereafter. Alexander Fleming rediscovered penicillin in 1928, but it was not until 1942 that Chain, Florey, and Jennings identified patulin, the antibiotic produced by P. glaucum . One can only wonder how the course of history might have changed if the value of penicillin had been appreciated earlier. Undoubtedly, there are many other solutions confronting each of us every day--if only we can find the problem!
Reformulation and revision: Great problem finders resist premature closure of the process of exploration. Scientific investigation is best served by a restless, self-critical mind. Gaps of understanding, disconnection between theory and clinical results, or anomalies in results can all stimulate new problems. Clinical scientists rarely reverse their opinions or point out their own mistakes because prestige, funding, and organizational power are at risk. Such forces may limit creative investigation. Great personal and scientific integrity is required to elevate new findings that weaken the theory on which one's reputation has been built. Yet without that acknowledgement and subsequent "course adjustment," investigation may continue down a blind alley and result in a career that is respectable but quickly forgotten.
Problem finding is an essential skill of clinical investigation, and the definition of a great problem sometimes occurs long after the solution has been observed. Relentless curiosity, the capacity to see the invisible, a willingness to reach outside one's own disciplinary silo, and continuous revision and reformulation are all components of the kind of problem finding you need to adopt to assure an important scientific career.
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2. M. Csikszentmihalyi, "The Domain of Creativity," in Theories of Creativity, M. A. Runco, Ed. (Sage, Newbury Park, Calif., 1990), pp. 190-212.
3. S. Rostan, Problem finding, problem solving, and cognitive controls: An empirical investigation of critically acclaimed professional productivity. Creativ Res J 7, 97-110 (1994).
4. A. Park, Judah Folkman, Cancer Pioneer . Time Magazine. Jan. 16, 2008.
5. S. Duckett, Ernest Duchesne and the concept of fungal antibiotic therapy. Lancet  354, 206 (1999).
6. E. Duchesne, thesis, Contribution a l'etude de la concurrence vitale chez les microorganisms: Antagonisme entre les moisissures et le microbes. Faculte de Medecine et de Pharmacie de Lyon (1897).