Chuck Sanders
Thirty years into my faculty career, I now sometimes play the game of “professionally speaking, what would I have done differently over the course of the years if I had a chance to do it all over again?” I don’t indulge in this exercise to second-guess myself or to stir up regret, but rather to ensure that lessons from my own experience can be passed on to those who will soon be making analogous decisions about their own budding careers in science.
It is in this spirit that I pen this highly subjective essay on choosing an independent lab project as an entry-level faculty member at a research university, or group leader in a research institute or government laboratory. This perspective is, no doubt, partly based on my own itinerary: all my training was in chemistry departments, while my independent career has been spent at two U.S.-based medical schools. Nevertheless, I hope these thoughts can be adapted for possible application to other professional trajectories.
The autonomy to choose and pursue projects of your own devising represents an EXTRAORDINARY opportunity in intellectual freedom. However, this does not mean all chosen paths lead to glory. An overarching objective should be to determine how to pursue the science that you find interesting while at the same time maintaining favored status with your employer, your peers, and your funding agencies.
Here are some thoughts on how to accomplish this:
- Choose a project where you will not be competing with your previous or current advisors. This does not necessarily mean that your independent project cannot in any way be related to your previous studies; however, it will not serve your best interests if the project puts you in competition with your Ph.D. or postdoctoral lab.
- Think outside the obvious boxes. Choose a project where you are not jumping into a field that is already crowded unless you are equipped to make a unique contribution.
- On the other end of the spectrum, there are virtues to setting off into a mostly empty frontier—you might even found a sub-field! However, there are also disadvantages to be aware of. If you are “out there” as the only person studying a particular system, it may be harder to find a community to plug into, and your papers may not get cited very much. This is true even for papers that prove, in the long term, to be very important.
- Consider choosing a “crossroads” project that addresses an area of science that represents an intersection between multiple fields. Such projects have unusual potential to be of high impact. A project that includes probing a basic protein science problem, involves a human disease, and is related to renewable biomaterials is an example of such a project.
- If you take a job here in the U.S. in a medical school, there will very likely be the expectation that by the time you are mid-career you should have two National Institutes of Health grants. The first of these could well be a National Institutes of General Medical Science “MIRA” grant, a popular program that has an early-stage investigator track. NIGMS is the main NIH institute that funds grants that are purely or largely basic science in nature. Because NIGMS now effectively has a one-NIGMS-R-grant-limit-per-investigator policy, your second project will probably need to have direct disease relevance so that you can seek funding for it through one of the more directly health-related institutes of the NIH (the National Cancer Institute, for example).
- Irrespective of the above point, it may be wise to choose a project that has direct medical relevance that can be pitched both to relevant disease foundations (which very often have funding programs for starting faculty) and to the NIH. Even if you are mainly interested in very basic science questions, there is likely an excellent, medically relevant system with which you can explore the very same basic science questions. Take time to do the extra homework to find and set up such a project. And you never know, your basic science work may eventually progress to the point where your results form the basis for therapeutic discovery!
- A good project for a starting lab should clearly be envisioned to be at least a 10-year project. You don’t want to be changing projects five years into your program. If the problems in which you are interested can be fully addressed in five years, then your project is probably of insufficient scope to be a project on which to base your lab.
- There once was a time where it was perfectly okay to define oneself as a scientist based on expertise in a particular method. I think this is much less true than it used to be. Even if you are really good at one particular method, it is now more important than ever to be biologically driven (or at least bio-savvy) in your scientific pursuits. (As I said, this document is highly subjective. It is perfectly OK to disagree with these points!)
- There is a place in your career for methods development projects, but very often such projects are not ideal as the theme of your first independent project—that is, unless the new method is being pursued in concert with the goal of leveraging the new method to solve a previously intractable problem in biology.
- It certainly is the case that your first project should be feasible based on the scientific tool-set that you bring with you into your early independent career. However, for long-term planning purposes, you can factor into the equation the fact that your skill set will be expanded as you go along by the tools trainees bring into your lab and/or by collaborations that you establish.
- Do be careful about relying on collaborators early in your career. Finding and maintaining good collaborations is one of the trickiest parts of science, and you don’t want to be overly reliant on collaborators for your early-stage success.
- As a corollary to the above point, realize that you are likely to be the best member of your lab during the first few years of independence, so factor your direct laboratory participation into planning for that first project.
- Inspiration for new projects can come in a variety of forms. In many cases it will be based on your mastery of the literature in an area of science you are interested in and/or a direction that seems obvious based on your training trajectory or the intersection between your Ph.D. and postdoctoral work. However, there are also methods that can be used to identify new projects. Twenty years ago, I compiled a list of human membrane proteins that were less than 250 residues in length and that are genetically-linked to human diseases. I then cherry-picked the most interesting 20 proteins and tried to express and purify all of them, abandoning the ones that failed to express well. This method eventually led to four different projects that garnered NIH grant support, two of which are still active 20 years later. I don’t claim this was a particularly scholarly approach, but it did lead to a lot of fun and interesting science. Other fertile territory for this sort of shotgun approach includes sifting through the results of screening experiments that identify molecules or pathways critical for a physiological or pathophysiological process.
- Grant proposals for good projects almost never die, but sometimes you really have to keep at it before a funding agency takes the bait. When possible, submit versions of your proposal to multiple agencies and take advantage of programs tailored for new investigators. Listen carefully both to colleagues and reviewers who give you feedback so that your proposal improves with each resubmission.
- Some grant program descriptions state that they do not require preliminary data, and they mean it. Others say they don’t require preliminary data but, in practice, do. Do your homework to find out which reality pertains, and factor the possible need for preliminary data into your planning. You can always negotiate with your postdoc advisor to see if they will let you collect some preliminary data for your future project before you actually start an independent position. Some newer grant programs like the NIH K99/R00 program are designed to seed your independent project even while you are a postdoc. (But if you are unable to secure a K99/R00 award, don’t worry. Lots of other scientists face the same disappointment but succeed anyway!)
- A suitable project around which to build your career should have an on-ramp that can be completed in a timely manner so that your project will start producing publishable results in time to support both professional promotion decisions (your tenure, for example) and eventual competitive renewal of your grant support for that project. So, think a lot about any barrier that must be surmounted before the productive phase of your project can be attained.
- When you start looking for your first independent position, your future research plans will be carefully scrutinized by your prospective future employers. I recall discussing this with my postdoc advisor many years ago and expressing my hope that universities are only truly interested in how meritorious the scientific plans are, not on the fundability of the project. Because my advisor was such an unfailingly positive person and not someone who volunteered a lot of advice, I have never forgotten his reply: “Don’t kid yourself, Chuck, it’s all about the money.” Appreciation of the reality of this statement has been very helpful over the years.
- Once you have accepted a permanent (independent) position but before you complete your postdoctoral studies, note that some funding agencies will let you go ahead and submit a proposal for the project you will pursue in your new position. If you can find the time, this is a great option to pursue and will impress your new boss (typically a department chair).
- Finally, let me add one additional comment about competition. As I noted above, avoiding relentless competition with other labs may be a priority when you choose your own project; it was for me. However, no matter what you choose to do there is always the possibility that you may get scooped. In this regard, I want to encourage you. Getting scooped is not always the disaster it often is construed to be. Yes, your work may end up being published in a lesser journal, but it very likely will still get published. And, you will be just as much an expert in your (evidently hot) topic area as if you had not gotten scooped. So just shake off the ghosts and move on!
Acknowledgement
I thank Raluca Cadar for her edits and helpful comments.