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Research serves to make building stones out of stumbling blocks.
—Arthur D. Little (1)
This is a time of the year when senior cardiology fellows are looking for life after they grow up! In discussing options with them, it seems that research, including that in cardiovascular imaging, is not high on their priority list. This is a major disappointment given that most of them, at their fellowship interview, all but swore to an abiding interest in a career in academic medicine. While we realize that there is always some strategy involved during the fellowship interview process, it is still an undesirable development for “progress of ideas” in imaging. This is clearly a frustrating paradox in that fewer and fewer cardiovascular trainees are choosing to become dedicated physician-investigators, at a time when the opportunities in imaging research are nearly endless. A major factor is quite likely the economic differentials among academic medicine versus private practice. Another, though less studied, factor might also be a perceived (or even real) lack of nurturing mentorship, and possibly, disillusionment with the day to day reality of imaging research compared to what they perceived it would be. With all these challenges, trainees are very unwilling, to paraphrase William Henry, to go on a blind date with knowledge. However, some of this might also be related to a lack of understanding about how to enter into and succeed as a physician-investigator. It might be apt to briefly summarize some of the current issues facing such trainees considering cardiac imaging research and possible solutions. A more comprehensive document from the Editors of iJACC will be forthcoming.
The importance of physician-investigators in research endeavors is undeniable and major advances in the past have involved teams wherein the physician-investigators were central to such efforts. On the other hand, much data show that this is a dying species in almost all major U.S. universities and academic medical centers. Imaging, with its predominantly clinical focus as well as clinical relevance, but with a relative paucity of funding for purely hypothesis-based research, is probably a field with a great need for physician-investigators as opposed to only basic scientists alone. The decline in physician-investigators is thus likely to hurt imaging-related research and innovation enterprise more severely. Efforts to bring in new physician investigators, who can ask and solve clinically relevant questions and generate hypothesis-based research in imaging is, therefore, an urgent priority.
Imaging is at an important juncture in medicine and is likely to increasingly dominate the fields of diagnosis, prognostication, and therapeutic strategy. While reimbursement issues may limit the speed of this trajectory, it is very likely to continue to be a major area of discovery and application. Newer fields of imaging technology and application (hybrid and fusion imaging, nanotechnology based imaging, biomarker imaging, functional imaging) and the fertile opportunities of cross disciplinary interaction (imaging informatics, imaging based statistical exploration and data mining, imaging based ethics, supercomputing, web sourced collaboration) will bring in even more opportunities for addressing difficult but fundamental questions. This will generate new low hanging fruit and also, hopefully, funding and avenues of funding will increase pari passu, to meet this need, albeit, to a lesser extent. Thus the footprint of imaging research will be wider and extend into areas not traditionally associated with imaging opportunities.
Such an opportunity should encourage physician-investigators, but how should an entrant view the field to be successful. Currently, imaging suffers from an excess of research into important, but rather modest impact questions—how to get a better image and how does this perform in detecting disease. There is a disturbingly scarce amount of inquiry into the wider patient related benefits of imaging. It is easy, therefore, for a young investigator asking “image and test performance” questions to feel good about his/her initial papers only to find the going very tough after that, when funding and career trajectory depends on performing a more substantial inquiry. Fellows should thus be educated early-on that all imaging research is not equal in terms of career and patient care impact (Fig. 1). This is a crucial issue to consider and, apart from personal traits predictive of success, where one enters into this field will make a big difference in how much success comes on the way and where one will end up in a career spanning decades (Table 1). Unlike in the past where a successful career could be limited to developing and testing a perfect image, it is a mistake now to concentrate on the image or modality by itself—to be successful, one should consider an image or a modality with respect to the environment or the company it keeps. One can think of an image as layers, beneath it (information on pathophysiology and biologic mechanisms) and above it (prognosis, outcomes, role in clinical care). Finally, it has information around it (how it relates to other clinical and imaging information) as well as other important dimensions (changing temporal and spatial and spectral dimensions, the so called fourth and fifth dimensions). Trainees should be strongly encouraged to try and find research questions that span across these layers; this not only opens up many more avenues for successful research but results from such research are more likely to provide a strong return on investment, i.e., alter patient outcomes and impact society.
Many obstacles exist and are likely to get worse in an environment of limited resources and greater accountability for those resources. Moreover, society places an oft-changing premium on the fields and tools used for research and discovery. Other deterrents include a constantly decreasing pool of funding, a mismatch of physician supply and demand, pressure to clinically generate salary, repayment of student loans, less societal value for protected research time during training and in early career stages, and a lack of freedom to choose research avenues (e.g., project-earmarked funding in case of commercial sponsors). Similarly, the very long period of training needed to master complex multimodal and multidisciplinary skills and technology, and less individual visibility in large research teams needed for complex trials renders a research career less attractive. Technologies change rapidly as does their role in patient care. Better prevention and treatment modalities reduce disease prevalence and in turn, low pre-test probabilities make improving test performance even more challenging. Thus, betting on a wrong imaging modality or question could result in an abrupt termination of an otherwise productive research career if one is not sufficiently cross-trained in skills and agile in approach. Finally, ever changing and decidedly more and more rigorous benchmarks that need to be met for getting reimbursements for newer technologies (e.g., the controversy associated with cardiac computed tomographic angiography) makes these technologies more controversial. Not surprisingly, this is a recipe for investigators to find themselves, as William Wordsworth put it for a different context, lost in a gloom of uninspired research.
Newer avenues that might open up opportunities
However, there is a very bright side to this reality too. Some new avenues that did not exist even a few years ago are now providing cross-fertilization in imaging (Table 2). These are areas we feel that would become dominant in the coming years; this could be a good start to a nascent career in imaging, providing a rare chance to learn new skills with the advantage of being some of the first researchers in this field. These areas are also likely to be the incubator for game changing ideas that are likely to impact career, the patient and society.
Strategies and suggestions
Not withstanding the fact that certain individual characteristics (a genuine interest to ask and answer questions, tenacity, and focus) are needed to succeed, some other learned strategies are also quite useful while thinking about imaging research.
It goes without saying that one needs to be well grounded in the basics of imaging before and during the research experience; knowing the strengths and weakness of each technique and how to critically interpret literature is vital to a good hypothesis and experimental plan. After that, the main elements of a good strategy could involve the following. First, the exchange of ideas is the most powerful tool one can harness in any research enterprise in general and in sophisticated imaging research in particular. As is often pointed out, our civilization itself was built on trade—trade of ideas and goods (2), without which one could not have progressed anywhere close to where we are today. It is, therefore, very important to join in the marketplace of ideas before starting an imaging research career and continually participate throughout the career, e.g., talking to different experts in multiple fields, visiting multiple labs, and actively participating in imaging society meetings. This should be coupled with searching relentlessly for good mentors, a highly productive lab to join, and finding helpful collaborators.
Second, it is also important, for a long lasting career in imaging, to think about the big picture and not focus on the image or the imaging modality alone. The new entrant should strongly focus on a story that imaging can tell and not a sound bite or a one-time punch line in that story. One cannot overemphasize that imaging research should primarily be considered as patient care too, the difference being that the rewards to the investigator, the patient, and society are somewhat delayed. Third, all imaging research has to have a patient care enhancer function; it is easy to get carried away with a pretty picture but that is a recipe for a short career, unless the research focuses on what it can do for the patient and society. Once this philosophy is internalized and digested, the next step is to identify an important problem to research. One useful suggestion, while not always possible, is to go away from the crowds if impactful research is to be the ultimate goal. It is interesting to observe people searching for a lost object in a darkened arena. Not surprisingly, everyone aggregates under the light of the nearest lamp pole, even though the chance of finding the lost object in that area is statistically quite small—the group logic here, albeit faulty, seems to be to look only in areas where we can see, where we find comfort from the unknown, and where we find others looking too. Similarly, research ideas tend to concentrate on what is easily visible and easy to do. Major breakthroughs, while rare and difficult to come by, have come from thinking outside such comfort zones. Even lesser discoveries in an unusual area or strategy, are likely to yield more important information than “me-too” kinds of studies. As Editors of iJACC, one thing we see very often is a premature rush to conclusion and publication without critical scrutiny. A healthy skepticism and asking a fresh pair of eyes to take a look is often useful; it is important to be correct rather than to be early.
Finally, it is easy to get discouraged and life provides an ongoing array of chances to get even more discouraged (e.g., a failed hypothesis, unexpectedly bad data, multiple rejections for a paper, or an unfunded grant). This can certainly be the death knell of a good research career. Having perpetual optimism is very important in imaging research. Experts continually predict the death of research enterprise as we know it, and a rejected paper often seems to amplify this message—as John Stuart Mill said, “… not the man who hopes when others despair, but the man who despairs when others hope is admired by a large clan of persons as a sage …” (3). Research proves time and again that this kind of sage is mostly wrong. The current depression about difficulty in doing research, difficulty in getting funding, and the idea that all low hanging fruit is already gone is absurd, especially in imaging research, where we are just starting out on a multidecade boom in technology.
Imaging research is very likely to be rich in opportunities and intellectually rewarding in the coming years, but physician interest for such a career choice seems lukewarm at best. We are loosing physician-investigators at the wrong time. The time window to develop a critical mass of new and highly trained imaging physician-investigators to harness newer possibilities in imaging appears to be finite and concerted effort is rapidly needed to encourage and retain new physician-investigators. Multiple issues including availability of nurturing mentorship, access to broad funding opportunities for clinical hypothesis based imaging research, a more conducive change in the strategic direction among funding agencies, and increased academic valuation for such research in academic medical centers will go far in making this happen. In addition to these structural changes, more active and targeted dissemination of crucial information (about strategies, opportunities, pathways, and exciting developments) to fellows in training will be useful. As Mark Twain would say, “supposing is good but finding out is better” (4).
- American College of Cardiology Foundation
- Little A.D.
- Ridley M.
- Mill J.S.
- Twain M.