I’m rarely in a comfort zone. Consider this career trajectory: mechanical engineering, then aerospace engineering, nuclear energy, solar and sustainable energy engineering, chromatography and NMR spectroscopy, biophysical chemistry, chemical engineering, molecular biology, and protein engineering. When colleagues caution me or dismiss moves as unorthodox and risky, my intentions toughen. Look, there’s a place in science for every personality. Mine happens to crave underwater caverns, snow-covered peaks, and high intensity, which is to say constantly changing territory. You may prefer peaceful, placid meadows. I’m not a bit intimidated by career peril. Temperaments vary.

I believe this decision depends on funds and opportunities on taking up your position. The ultimate aim is challenging projects. If good startup funds and support are available, delve into impactful big picture projects. If they are not, start with incremental problems to establish credibility. Apply for external resources. In the long term, pursue impactful projects.

My best advice here is to follow your data. Even in areas you thought already familiar, interesting data give rise to new questions. Expand both by applying the latest experimental or analytic tools available to you, or more affordable analogues if necessary. Knowing the evolutionary direction of emerging technologies is crucial. To familiarize themselves with these, students and postdocs talk to sponsoring vendors at conferences. Everyone including me also track this information by following the literature very closely.

I always have long-term, challenging goals as well as short-term, low-hanging fruit projects. One has to be publishing regularly by doing several things at once.

It’s hard to predict what will be “big-picture” and what will be “incremental.” Projects must be achievable, so practical considerations might mean that though one idea is attractive and challenging, and another less so because its day-to-day work is more routine, you simply have to get something done. In any case it’s not a good idea to take up a project too close to your previous mentors’. Most important of all is identifying a problem that interests you and thinking very carefully how to attack it in the most practical way possible.

You are under scrutiny from day one. For this reason, a combined approach might be the smart choice; then, as soon as you can, leave the comfort area whose challenges are known. Remaining in it does not bode well among those who assess you. Adopting a niche area of your own is essential to getting your foot in the door and making your mark. Taking from my own example, I analyzed protein-protein interactions for my graduate studies. All the work was theoretical, based on statistical analyses, but I decided that my own laboratory would also have experimental operations. Having done nothing like that in the five years of my doctoral work either this was not easy to arrange, but now, when I look back, I believe I achieved a successful laboratory.

In my opinion a combination giving stronger emphasis to innovation is most productive in an academic career. To be considered active as a professor, it is important to maintain continuous publication of papers. Incremental innovation in an area you already know permits this, but it is also mandatory to start impactful work in different scientific areas to keep you curious, highly motivated, and to attract younger collaborators.

On starting my independent career, I left biochemistry, the area in which I trained from college through my post doc, for the field of medical research where I remain today. Naturally I applied much that I had learned to the new area, so the most accurate answer is “both combined”.

Big risky problems are best, but it is advisable to have both risky and reliable research running in parallel. When I started, I have to admit, I was not that strategic.

For me impulsivity proved timely. Thanks to gains in processing power, even our bluest-sky ideas exploded like fireworks, but that electrifying light overshadowed small signs of trouble waiting to be seen. Successfully straddling supportiveness and caution takes time to learn, as do the subtle differences between hope and desire. Science operates on hope: on curiosity seeking satisfaction, and efforts to understand, as ends in themselves. These are pure aims. Desire for recognition is different. It’s unholy and the ultimate heartbreak. Guard against overreach and grandiosity by lab book swaps and critique, group problem sessions, and group meetings that probe more deeply than pro forma.

If the chosen project/topic is not sufficiently challenging, it is difficult to get grants, but high-risk projects often fail to give short-term returns and publications. Therefore a combination of high-risk and bread-and-butter projects seems best.

It is in academic researchers’ DNA to challenge comfort zones. Though science today is global, local academic cultures are diverse enough that a young scientist must be attuned to internal, external, and international research directions, collaborations, interpersonal mixes, and funding sources. The successful new professor combines personal expertise with keen lateral awareness.

I was recruited as a lecturer and am now a full professor. Thus I have walked the full path. As a department chair I advised new researchers as follows. During the first years until you get tenure, pursue two lines of research, one in which you have proven skill and is the reason you were recruited; and a second that is ambitious. The comfort zone creates a solid basis for publications. Once you are successful and secure tenure, the sky’s the limit. Leave your comfort zone.

For me a combination has worked well. While I still love my Ph.D. and postdoctoral fields and topics, I have also found it useful to extend into other areas. Reciprocally I bring their new ideas and applications back to the original work. The job of P.I. requires stepping to the next level, tackling bigger-picture projects, and finding your own approaches, ones that don’t repeat and follow your former advisors. Stretch out of the comfort zone.

In my experience it is most effective to undertake a challenging, impactful big-picture project. It takes more work and is, to begin with, perhaps less productive in terms of scientific papers and other tokens of success, but it does pay off in due course. Eventually your research is more widely read and a greater number of young people want to work with you.

I advise a portfolio of projects at different risk levels. In general, I prefer to publish fewer papers but in higher impact journals; and I prefer to read papers that tell a full rather than incremental story. I try to avoid the “least publishable unit.” That said, early on it is good to start getting papers to press, possibly following the strategy of publishing a proof-of-principle study that doesn’t “self-scoop” a later, bigger-impact publication. In my opinion, you need a few papers early on to get grants: at least one good preliminary result per aim, in the United States, to demonstrate proposal feasibility. Use your institutional support to get those results! Early in your career, patents are not as important for advancement.

After doctoral studies in synthetic organic chemistry I chose a career in the same field. As a professor I teach organic chemistry to undergraduates and postgraduates; in research I am always looking into how to apply what I know to challenging projects. I believe it is important on starting a career to choose the field where solid foundations were acquired and comfort is felt. Over time, on building up experience, look into more challenging projects that can be impactful in the scientific community and also help you evolve as a scientist.

Think of your research program as you might an investment portfolio. Combine reliable instruments yielding low to medium but steady profits with high-risk, possibly high-yield investments.

When I was an assistant professor I wanted to move into the completely new area of DNA nanotech but was concerned about tenure. I maintained two streams in my lab. One related to my previous training, which gave me enough productivity for tenure, and the other was a longer-term project in the new area. Today I work in a field very different from my early training but bring the training to it.

In my first jobs, the choices implicit in this question were inconceivable, at least in my case. There were few if any negotiations, options, packages, career planning, or signs of interest in the first, usually the only, woman hired. The whole hope was for good fortune in receiving any job. Plus side: when attention or curiosity run one-way for the most part, from you to colleagues and not reciprocally, you’re essentially on your own, free to be drawn into whatever bold, hard, knotty questions you like. I wrestle with rigorous, careful explanations of big problems as scientific trends come and go elsewhere. That’s what I’m known for. That’s what it will say on my gravestone.

The answer to this question really depends on what you want to achieve and in what kind of atmosphere. Many researchers have satisfying careers making incremental advances. Providing the questions are of significance, this can be rewarding and perhaps allow for a side bet on something big, but such a play it safe strategy will likely not net you a career in a top research school. You can succeed at a lower-tier good-quality college or university, perhaps balanced with (hopefully satisfying) teaching, or at a national laboratory for full-time research in a good environment. If, on the other hand, if you want a top research school and prizes, you pretty much have to embrace a big challenge. A recent memoir on solving the ribozyme structure by Venki Ramakrishnan illustrates what is required: a combination of obsessive drive and plain good luck. High risk, high reward. For myself, I was always most interested in refining research methods, but recognized I had to convince funders I could answer important questions. I chose problems that made the case for methods being central to results, which worked for me.

After being promoted to associate professor, I started a new working group, a Laboratory of Anaerobic Microorganisms, and a new research program. Serving at the same time as head of a larger Microbiology Department, I saw that it is important to maintain diversification among all our various research groups.

All research demands dedication, and maintaining quality is key at every level, but full articles serving an ambitious overarching aim are my personal preference and goal. I want, and wait to publish until, stories are as large and complete as I can make them.

The most important factor here is focusing on a problem that interests you. Namely, be driven by your curiosity.

My strategy has been to balance the two complementary streams. I pursue one safe in the sense of being straightforward and productive; as well as the second, which is risky but possibly more impactful.

As an assistant professor I undertook an entirely new area, and have remained there. From mechanical engineering as an undergraduate, graduate student, and postdoc, I went to tissue biofabrication and drug delivery.