Mark B. Kristal's Suggestions for a Basic Research Career

It's rare that I encounter advice that's pitched at exactly the right
level for where I'm at in my life/career. This is such advice, and struck
me as excellent.
http://www.psychology.buffalo.edu/essay.shtml

Here are the best bits that I took away from it, in case this is taken
down:

--

* Establish an independent line of research as early in your career as
possible. If you can, do so even as a graduate student. Avoid the graduate
student's trap of thinking up experiments in other researchers' programs
that the other researcher has missed. Of course these are useful studies,
but do not form the basis of one's own independent line of research.
* Be problem-oriented, not technique-oriented. Use a variety of
techniques,
methods, and orientations -- whichever are necessary to solve the problems
at hand. Remember, technology comes and goes, but the underlying
questions are the meat of research. It is depressing to go to poster
sessions at the big conferences year after year and see the same questions
being asked over and over with different, more .cutting edge. techniques,
presented by people enamored of the techniques rather than the research
problems. If technology is so costly, in terms of equipment, learning
time, and other resources, how does one avoid the trap of becoming
technique oriented? The answer: collaborate.
* Think beyond the next publication, or even the next grant proposal. Take
the long view; look at the big picture. In other words, bite off a piece
of question that may take a decade, or even a career to answer. There is a
major difference between the scientist that wonders how to break the
question into appropriate sized grant proposals, and one who wonders how
to expand the question into a grant proposal. Furthermore, commit yourself
to your question; given the time and energy it takes to answer an
appropriate sized research question, pursuing a series of unrelated
research questions in parallel rather than in series is often a sign of
dilettantism.
* If you do basic research, keep your eyes open for applications of your
findings.
* Don't expect answers; expect more questions. Daniel Lehrman used to tell
us that a good experiment will raise more questions than it answers.
Perhaps non-scientists find this aspect of science strangely frustrating.
However, the lack of a final solution distinguishes the scientist's quest
from the engineer's.
* Never stop asking questions.
* Choose a problem that excites you. It should excite you so much that you
can't sleep. It should excite you so much that when someone asks you the
time, you blurt out your research topic.
* Strive for elegance in research. The elegance of an experiment is in
the quality of the thinking and the cleverness of the approach to
answering the research question, not in the complexity of the design or
the sophistication of the methods. Often, the most elegant experiments are
simple, low-tech attacks at the heart of the problem. Study classic
research in your field and appreciate the logic and thought that went into
it. All too often students nowadays ignore older research because it isn't
available online, or dismiss it for using old-fashioned techniques. There
is much wisdom and cleverness in some of those old papers. Reading them,
learning from them, and citing them, is real scholarship.