by Professor Kenneth Hanson, Florida State University
In my last post, I focused on the transition between being a postdoc
and professor. In this post—the second in the
“Keep Your Job, Ken!” series—I
share my thoughts on choosing a research direction and advice for short- and
long-term success.
1) While it helped
you get the job, you don’t have to pursue the research you proposed. Maybe
between the interview and the start date you get scooped, or learn why your
proposal won’t work, or become interested in a new area of research. Either
way, you have a lot of flexibility. Once your startup account is set up the
funds are largely unrestricted and no one is keeping track of what you spend it
on (at least within reason. i.e. don’t try to buy a trampoline). You were also likely
hired based on who you are as a person and the general area you work/teach in.
Very few of your colleagues will remember your proposals and those that do will
most likely have no strong opinions regarding whether you pursue them or not.
2) Make sure to
clearly differentiate yourself from your graduate and postdoc advisors. We
spend several years of our graduate and postdoc careers becoming an expert in a
particular area. It can therefore be exceptionally easy to stay in that groove
and continue on. However, I strongly recommend avoiding the trap of postdoc 2.0.
That is, if your first pursuit as an independent researcher is a natural continuation
of your postdoc work (i.e the first paper you publish independently could also
have been the next paper in your post doc), don’t do it. It would technically
be an independent publication but the community at large will very likely not consider it to be original work. You
need to carve out your own research identity. In fact, many of the young
investigator grants (i.e. NSF-CAREER, ACS-PRF NDI, and others) ask reviewers to
comment on how the proposed work relates to a candidate’s previous advisor. Even
for some non-young investigator
grants that didn’t ask this specific question I’ve seen reviewers’ comment on
the relationship of the work to my postdoc and grad advisors. This question is
clearly on people’s minds and if your work is too similar then it can be a
death knell for your proposal. Ask yourself, if I was going to fund a project
or invite a speaker, why wouldn’t I go with the person who started the work rather
than the person continuing it? I completely understand the appeal of low
hanging fruit and easy papers but this time and effort could be better invested
in producing preliminary results for a unique pursuit and fundable proposal.
There is a blurry line between being too similar, being independent, and
deviating too far (see point 4). Here’s an activity you can do to help assess
your own trajectory towards differentiation: list the titles of your postdoc
papers and then, next to it, the title of your proposed paper(s). If a member
of your field could not differentiate your paper from those produced under your
previous advisor they are too similar.
3) Work to define your
niche in the community at large. While minimizing your overlap with
previous advisors, you also want to make sure you’re not mirroring someone else
in your field. Ideally, your work should be unique enough to be cited in another
person’s paper as a notable step forward (i.e. Dr. Doe et al. showed that…) and
not just in the list of publications. When you write a proposal you want
reviewers to see you as uniquely positioned to pursue the project. Also, when
your tenure letters come in, you want them to read “Dr. Jane Doe is the world’s
foremost expert at X.” The more encompassing X is, the more impactful the
statement is. You don’t want it to say, “Prof. Jane Doe expanded/improved on
the work of person Z.”
4)
Balance high risk,
high reward projects with guaranteed projects. We all dream of, and
sometimes get, those coveted
Science
and
Nature papers. But they are hard
to come by. In addition to
impact,
the total
number of papers also matters
for grants, awards, and tenure. Therefore, it is risky to put all your eggs in
one or two precarious baskets. Those projects/ideas are worth pursuing but
should be supplemented by projects that are basically guaranteed to result in a
publication. Studies that systematical vary one or two parameters (e.g.
solvent, sterics, instrument setting/components, etc.) can be a bit tedious but
can also provide a foundation for yours and others’ future work. These
manuscripts will typically not land in
JACS
or Chem. Sci., but they are guaranteed a publication in more
specialized journals. Also, depending on the topic, it may accidentally be one
of your higher cited papers. For example, my postdoctoral
JACS article on a new bisphosphonate decomposition mechanism
has 8 citations but my
JPC C article that systematically varies
surface bound phosphonated dyes has over 100 citations. As a side bonus,
these projects can serve as rigorous and systematic training for your graduate
and undergraduate students and boost their proficiency at a particular set of
measurements, procedures, and/or reactions.
5)
Try not to wear
yourself too thin. You no doubt have many good ideas and projects that are
worth pursuing. That is part of the reason we chose this job: We are in love
with our own ideas and want the flexibility and freedom to pursue them. However,
time and resources are limited. Just like in warfare, a concerted front may be
better than a diffused attack. Focused research helps produce a solid
foundation of preliminary results necessary for a proposal. It also helps carves
out a niche that can get you invited talks at specialized conferences. As a
bonus, a focused effort gives you a good story rather than a gathering of
factoids to tell during your tenure tour and departmental seminar. With all of
that said, I am a bit of a hypocrite for advocating for focused research
because we have published work in controlling
interfacial electron
transfer,
photon
upconversion,
photochemical
separations, and
enantioselective
excited state proton transfer. Not exactly the most focused of research
efforts. I wouldn’t say I regret any of our work but it might have been more
effective to narrow our focus a little bit. I think the take home message I’m
trying to get at is that there has to be a balance between putting all your
eggs in one basket and becoming too diversified.
6) Collaborate…or
don’t. I have received mixed feedback on the subject of collaborations
before tenure. Some are strongly opposed to it. Others don’t care. The best
path is probably somewhere in between. The advice I ended up following was to
collaborate as much as I wanted as long as I had an independent research
pursuit and/or it was easy for an external viewer to delineate my contributions.
For our photon upconversion and excited state proton transfer work, for
example, we had almost no collaborators prior to tenure. But I also had a
number of collaborative papers where my contribution—providing photophysical
support—was obvious.
7) Make the
transition out of lab as quickly as possible. For the first year or so
there is no question that you will be the best postdoc you could ever ask for.
Given your experience and expertise you can hammer out a few papers very
quickly and with minimal effort. However, this is a short-term strategy. It is
only a matter of time, usually around year 3, before other responsibilities
(i.e. committee duties, proposal writing, teaching, etc.) will force you to
significantly cut down or eliminate lab time. Therefore, it is important to
spend that initial lab time training students and making them self-sufficient
as quickly as possible. In line with the proverb "If you want to go fast,
go alone; if you want to go far, go together." This is hard to do because
it requires us to step back and watch our students struggle and make mistakes
as they learn. Progress will start slow, but it will be worth it in the long
run, especially considering the students you train will then go on to train the
next generation of graduate students. Also, the sooner you trust your students
and let go of lab work, the sooner you can dedicate yourself to writing
proposals.
