Introduction In the course of my career, I have been asked, "How did you become a full Professor at Stanford University before the age of 42?" Here are my best answers: My parents. Because they were (and remain) scientists, I was exposed to academia at an early age. I recall overhearing impassioned and serious discussions about journal articles and grants before I was able ride a bike. Later when I joined a faculty, my parents became unbiased mentors, providing unqualified support, as well as practical advice. My wife, Susan. When I first met her during medical school at the University of Rochester, she worked in the medical center as a technician in the intensive care unit and cardiology laboratory. Her occupation gave her valuable insight into the demands of clinical practice in a way that no one can know outside a hospital setting. For example, she was acutely aware of the physical and emotional toll that being on overnight call can bring, what an intensive care unit looks like, and what sacrifices and demands of being a medical practitioner would mean to our family life. With her consent and support, I was able to work the long hours required to succeed as a faculty member and family man. Good luck. I was fortunate to have finished business school in the late 1980s, which gave me the right set of analytic tools to address economic questions pertaining to clinical practice just as interest in the field of health economics was taking off. Mentors. I was hired into a nurturing department with phenomenal mentors and superiors at such an outstanding university as Stanford. Having a strategic plan. I loved learning about why things work the way they do, so what better way to satisfy this curiosity than to teach and do research in that field? Many paths can lead to becoming a successful physician-scientist. Below I describe one that worked for me. Choosing a Research Area I encourage physicians in clinical practice at teaching hospitals to pick an academic area that is directly related to their everyday patient care responsibilities. This may seem obvious, but it is easy to overlook. In my case, I chose to work in the operating room, providing anesthesia for orthopedics and ambulatory and neurosurgery cases. In addition, I spend 1 week a month organizing staff (faculty and residents) so that they are optimally assigned to take care of patients scheduled for surgery. My research is generally in those 2 areas. I came of professional age at a time when medicine was becoming a business, and many questions and research opportunities on the business side of medicine arose. Seeing my research interest firsthand provided me with material for asking the appropriate questions. Providing patient care, answering consults from others, and teaching others what I have learned and am studying makes me a better researcher and clinician. Pick an academic area that has attracted little attention. If you have only 1 day per week for research, and you choose the same research area as someone at another university or in another country who is able to devote 4 days per week to research, then you will have a tough time getting ahead. The downside is that funding for an understudied area can be more difficult to obtain. Don't put all your eggs in 1 basket -- select 2 or 3 (related) areas of investigation as insurance. In my case, research in operating room management was the area that no one was working on when I started, but the downside was that federal government, industry, or other funding for this area was limited. As a backup, I developed an interest in the economic assessment of new drugs and devices for use in surgical patients. This became a second line of investigation and was more likely to be funded, but many other investigators were already busy doing similar cost-effectiveness analyses The Research Question Keep your ears open for questions generated by colleagues, or even by patients. "Why do you do this?" or "Why does that happen?" could be questions that lack properly tested answers. The best questions lead to solutions that help patients. It is wise to devote time (much more than you think you should) to formulating a strong research question. It is imperative that the research question can be answered with currently available methodology and that the answer will lead to a peer-reviewed publication. The journals will assess whether the study is interesting (if the study is perfectly executed but boring, no one will care), valid (if study is done incorrectly, then no matter how new or interesting the subject, it will not get far in peer review), and new (a study could be interesting and valid, but if a similar study was published recently, yours will probably be rejected). Physicians are not typically trained as scientists, so aspiring clinician-scientist faculty now need at least 2 years of dedicated training in research methodology. The rigor and sophistication of the required research methods increase every year. Back to the research question: If you pick the wrong question, then no matter how strong the methods are, you will have wasted valuable time and will have not produced answers from which the scientific community, physicians and nurses, and society can benefit. The same is true if you select an appropriate question, but the available methods don't allow the question to be answered. This is where a mentor can be helpful, by putting your research interest in the proper historical context and helping you see where the gaps are in what is already known about your topic. One must be deeply curious and passionate about the research question to succeed. Neophyte scientists often aim to answer a question that is too difficult or too broad. I was guilty of this! When I first started writing grants, I thought I had to hit a home run (make that a grand slam!). I believe I thought, subconsciously, that for a sponsor to give me money to study something, the subject had to be really big (which leads to being too broad). This resulted in the research design being overly complicated and execution of the protocol daunting. Now, I believe something less ambitious and of less risky scope is the wiser course in obtaining funding. Granting agencies are not in the business of speculating. In other words, entities that give money for research are risk-averse -- they are looking for a definite return (eg, published data or notoriety) on their investment. As a beginning junior faculty member, a research project you might consider too simple and basic will give you the opportunity to start something, exercise your research and analytical skills, become facile with the institutional review board process, obtain informed consent from patients, and try manuscript writing. By taking baby steps, you can acquire competence in each stage of research. You can then move on to larger, more complex projects. Tackling too big a project early on can lead to frustration and burnout. When possible, use existing datasets to do research. Lots of data already exist, so be on the lookout for databases to analyze. Obviously, retrospective audits of such databases have limitations, but in most fields, observational data are useful for evidence. I believe the cost (time, energy, and frustration) of primary data collection is very high, and it should be reserved for the most crucial projects that cannot be answered any other way. Also, randomized, controlled trials have exclusion criteria that may limit the applicability of findings to the general patient population -- an unsatisfying outcome. Which datasets already exist should be a factor in helping you decide which research questions to pursue. Anesthesia information-management systems and electronic medical records come with loads of data. Certainly, a growth niche for future research in anesthesia will be how to properly query, analyze, and use such data. Keep in mind that it is better to be approximately correct than precisely wrong,something I learned in business school at the University of Rochester. To grasp this fully, imagine that you are trying to calculate the cost of operating room time to the hospital. To illustrate how you could be "precisely wrong" when studying this question: You might collect all the items used during surgery and anesthesia; determine, to the penny, the charges billed by the hospital to the insurance company for each item; and then put it all in a spreadsheet, with a final total. The answer would be precise, perhaps even to the 1/100th decimal point. However, the analysis would make at least 2 key mistakes: (1) Charges as they appear on the hospital bill have no relationship to actual hospital costs, and (2) most operating room costs to the hospital are related to overhead, such as the mortgage payment for the hospital building, which will be fixed regardless of how many cases are performed. It would be much better to be "approximately correct" and answer this question with estimates of hospital acquisition costs for supplies and labor and estimates of the fixed overhead costs allocated to the surgical suite. Don't forget that small differences in very precise measurements may be statistically significant but of no clinical importance, whereas large differences may be clinically important, even if they do not reach statistical significance. Another lesson to learn is that each medical school, department, and hospital has individual strengths. Some places have the systems and people to analyze administrative data really well but don't have the culture to do small clinical studies well. Part of the aspiring physician-scientist's formula for success is figuring out your institution's strengths and learning how to leverage them. Swimming with that tide will carry you farther. Staying on as faculty after residency at the place you trained clearly gives you the advantage of not having to relearn the culture. Moving to a new academic medical center to initiate an academic career is difficult, because it takes at least 18 months to get a physician-scientist up and fully running at a new department. Promotion As an Assistant Professor, the question may come to mind, "What must I do to get promoted?" Having been at a single medical school for 15 years, I have seen these criteria change over time in both major and minor ways. What is true today about what you need to be promoted may not be true 10 years from now when you are being judged. I encourage junior faculty to focus on productivity (getting things done) and not on worrying too much about such questions as, "Do I have what it takes to get promoted?" Dwelling excessively on this question wastes emotional energy and time that should be allocated to professional development and ongoing scholarship. Faculty promotion at medical schools, such as Stanford, primarily rewards research and scholarship. At many such research-intensive medical schools, faculty in the research track (either clinical- or laboratory-based) are not rewarded by promotion for many other generally worthwhile professional activities, such as being on an admissions committee or directing a new curriculum. It is very tempting to engage in such activities in part because you want to be a good citizen of the medical center and school. However, these activities take time away from the laser focus on research required to have a chance at being successful. The exception to this guideline are nonresearch activities that are directly related to your research area. For example, if you are studying how to make the hospital greener and more environmentally friendly, and the hospital has embarked on a quality improvement project on operating room waste, then you should try to get on that committee. At the same time, I encourage people to publish as much as possible, even if the publications are small, and to do so as early as possible. The default should be that every activity the young professor engages in can be written up, until proven otherwise. Again, this "stretching of the legs" is practice for the future when the more extensive papers are written up. Certainly, there is great pleasure and satisfaction in seeing an article you are particularly proud of finally get in print! During a time of initial faculty appointment and again with promotion, the number of one's peer-reviewed publications is simply counted, without specific examination of the quality of the work. Although this may be disconcerting to the potential faculty member, the reality is that it is impossible for the individual who is evaluating résumés to be an expert in fields as disparate as molecular biology, radiology, and pediatric hematology, for example. As a result, reviewers resort to counting papers, and they then rely on leaders in the field to confirm the candidate's overall caliber and stature. Nor do resume reviewers look only at whether one's publications are in The New England Journal of Medicine, the Journal of the American Medical Association, or Science,because many high-quality articles are published in high-impact journals in each of the dozens of specialties. Portfolio of Projects Small projects can unexpectedly become big ones. As a resident in the mid-1990s, I did a straightforward study with Dr. John Brock-Utne, looking at the degree to which anesthesiologists underestimate the volume blood in surgical sponges. Ten years later, this became a National Institutes of Health (NIH) Small Business Innovation Research grant on radiofrequency identification tagging of sponges. Never in a million years could I have predicted this! I encourage young investigators to have a portfolio of projects: Some should be low-risk/low-yield (such as a literature review, because you know it can be done), some medium-risk (such as a questionnaire/survey study; this requires human subjects approval and development of a tool, but it is likely to get done if you put enough effort into it), and some high-risk projects but with higher yield. By high-risk, there is some risk of the study not be completed or not being published, because the methods are unproven, or it is uncertain if the data can be properly collected. On the other hand, if you do finish such a project, it could result in an important article. Team Research Find people who are smarter and harder-working than you with whom to collaborate. In my case, that was Frank Dexter, an academic superstar. Research is done by teams now, much more so than in the past, and the team members can be anywhere in the world. The Internet allows very specific expertise to be brought to the table. Some people are really proficient at getting the paperwork in for human subjects approval; others don't like doing human subjects-related work but are good at getting informed consent and enrolling patients (something I was never good at). Others are experts at statistics, some at getting funding, and still others at writing. Division of labor, if managed correctly, yields more productivity. However, the downside is that your academic career depends on others, so work with the best people you can find. Spend 20% of your academic time promoting your work to others. With email, this is easy. When you finish writing a manuscript, send the draft out so others know what you are working on. Go to scientific meetings. Introduce yourself to the players in your area and cultivate relationships with them. Try to find something to collaborate on. Here's another pearl: underpromise and overdeliver. I thank Dr. Terry Vitez for articulating this point to me when I was first on faculty. What did he mean? Let's say you promise someone you will finish project X by time Y. Then, deliver X multiplied by 2 (twice what you said you were going to do) way ahead of time (Y minus weeks or months). The person you are delivering this to -- mentor, boss, journal, funding agency, collaborator -- will be so jolted by your efficiency, that the next time they need something, they will call you! You will suddenly find yourself involved in lots of fun things. Grants After most of my early grants were rejected, I realized that NIH funds are predominantly geared toward chronic disease research, such as HIV/AIDS, chronic lung disease, asthma, and congestive heart failure. Anesthesiologists generally deal with acute disease, so this disadvantage often materializes when applying for federal funding. The anesthesiologist in academic practice does have one advantage -- the nature of operating room anesthesia work. Responsibility for the patient is mostly finished when the patient is discharged from the recovery room. This freedom will help academic productivity. Looking back, I did well networking with investigators in my field, but I did not do enough cultivating relationships with the officers at the NIH study sections. Find out what the people who have money for research want to fund. Speak to the administrator at the NIH or the industry sponsor to see if they are interested in your idea. You could write a terrific grant application about exciting topic X, but if the agency wants to fund topic Y, your chances of getting a positive response decline. Make sure you can meet or exceed their needs. Look closely at what they have funded in the past rather than relying on what they say they want to fund in their marketing materials. Getting used to rejection (papers and grants), is necessary, although not easy. Writing Write papers a little bit at a time. To sit down and write an entire paper on a Saturday morning is impossible. Different approaches work for different people. What I do is if I read an article in a journal that is related to my general academic interests, I immediately record the take-home message and the reference in a Word document. Also, when I have a spontaneous and hopefully original or creative thought on the issue, I add it to the same Word document. Soon, I have a document several pages long. I continue building elements of the paper piece by piece, and then I send it to colleagues for comment in the draft stage. One useful endpoint for full-length manuscripts is to always think in the context of having to write a review paper on the current state of your area. Then, it is easier to decide what studies need to get done next, either by you or others. Final Thoughts If I can do it, you can do it. A physician-scientist uses his or her clinical experience to inform the research question. Being an outstanding investigator is a full-time job, as is being an outstanding clinician. Being outstanding in both is a challenge. Perhaps most important is a happy, supportive home situation. I was very fortunate here. In my case, my wife opted to stay home while we had young kids (she returned to part-time work a few years ago at the local elementary school) so that I could get papers done on nights and weekends. Worrying about not having enough money to pay the bills can pose the risk of doing more clinical work, which eats into academic pursuits. Everyone talks about the importance of mentors, but building the relationship is the mentee's responsibility. Mentors will respond if the mentee is successful and delivers something to the mentor. I find mentors particularly useful for deciding when to say, "No, thank you." Staying sane and healthy professionally and personally requires saying "No, thank you" to lots of things that seem worthwhile but detract from your primary focus. I think an academic career can be hugely rewarding and offer mind-boggling variety in the course of a career. You can be a researcher for a time, then an administrator in the dean's office, or teach an undergraduate course, all under the same employer! Finally, if at all possible, start a fellowship program so that young, hard-working people can join your team. Time and attention are required to help them along, but the reward is worth it. Source
