Always Prepare for the Worst.
Some of the greatest catastrophes in graduate
education could have been avoided by a little intelligent foresight. Be
cynical. Assume that your proposed research might not work, and that one of
your faculty advisers might become unsupportive - or even hostile. Plan for
alternatives.
Nobody cares about you.
In fact, some professors care about you and
some don’t. Most probably do, but all are busy, which means in practice they
cannot care about you because they don’t have the time. You are on your own,
and you had better get used to it. This has a lot of implications. Here are two
important ones:
1. You had better decide early on that you are
in charge of your program. The degree you get is yours to create. Your major
professor can advise you and protect you to a certain extent from bureaucratic
and financial demons, but he should not tell you what to do. That is up to you.
If you need advice, ask for it: that’s his job.
2. If you want to pick somebody’s brains,
you’ll have to go to him or her, because they won’t be coming to you.
You Must Know Why Your Work is Important.
When you first arrive, read and think widely
and exhaustively for a year. Assume that everything you read is bullshit until
the author manages to convince you that it isn’t. If you do not understand
something, don’t feel bad - it’s not your fault, it’s the author’s. He didn’t
write clearly enough.
If some authority figure tells you that you
aren’t accomplishing anything because you aren’t taking courses and you aren’t
gathering data, tell him what you’re up to. If he persists, tell him to bug
off, because you know what you’re doing, dammit.
This is a hard stage to get through because
you will feel guilty about not getting going on your own research. You will
continually be asking yourself, “What am I doing here?” Be patient. This stage
is critical to your personal development and to maintaining the flow of new
ideas into science. Here you decide what constitutes an important problem. You
must arrive at this decision independently for two reasons. First, if someone
hands you a problem, you won’t feel that it is yours, you won’t have that
possessiveness that makes you want to work on it, defend it, fight for it, and
make it come out beautifully. Secondly, your PhD work will shape your future.
It is your choice of a field in which to carry out a life’s work. It is also
important to the dynamic of science that your entry be well thought out. This
is one point where you can start a whole new area of research. Remember, what
sense does it make to start gathering data if you don’t know - and I mean
really know - why you’re doing it?
Psychological Problems are the Biggest Barrier.
You must establish a firm psychological stance
early in your graduate career to keep from being buffeted by the many demands
that will be made on your time. If you don’t watch out, the pressures of course
work, teaching, language requirements and who knows what else will push you
around like a large, docile molecule in Brownian motion. Here are a few things
to watch out for:
1. The initiation-rite nature of the PhD and
its power to convince you that your value as a person is being judged. No
matter how hard you try, you won’t be able to avoid this one. No one does. It
stems from the open-ended nature of the thesis problem. You have to decide what
a “good” thesis is. A thesis can always be made better, which gets you into an
infinite regress of possible improvements.
Recognize that you cannot produce a “perfect”
thesis. There are going to be flaws in it, as there are in everything. Settle
down to make it as good as you can within the limits of time, money, energy,
encouragement and thought at your disposal.
You can alleviate this problem by jumping all
the explicit hurdles early in the game. Get all of your course requirements and
examinations out of the way as soon as possible. Not only do you thereby clear
the decks for your thesis, but you also convince yourself, by successfully
jumping each hurdle, that you probably are good enough after all.
2. Nothing elicits dominant behavior like
subservient behavior. Expect and demand to be treated like a colleague. The
paper requirements are the explicit hurdle you will have to jump, but the
implicit hurdle is attaining the status of a colleague. Act like one and you’ll
be treated like one.
3. Graduate school is only one of the tools
that you have at hand for shaping your own development. Be prepared to quit for
awhile if something better comes up. There are three good reasons to do this.
First, a real opportunity could arise that is
more productive and challenging than anything you could do in graduate school
and that involves a long enough block of time to justify dropping out. Examples
include field work in Africa on a project not directly related to your PhD
work, a contract for software development, an opportunity to work as an aide in
the nation’s capital in the formulation of science policy, or an internship at
a major newspaper or magazine as a science journalist.
Secondly, only by keeping this option open can
you function with true independence as a graduate student. If you perceive
graduate school as your only option, you will be psychologically labile, inclined
to get a bit desperate and insecure, and you will not be able to give your
best.
Thirdly, if things really are not working out
for you, then you are only hurting yourself and denying resources to others by
staying in graduate school. There are a lot of interesting things to do in life
besides being a scientist, and in some the job market is a lot better. If
science is not turning you on, perhaps you should try something else. However,
do not go off half-cocked. This is a serious decision. Be sure to talk to
fellow graduate students and sympathetic faculty before making up your mind.
Avoid Taking Lectures - They’re Usually Inefficient.
If you already have a good background in your
field, then minimize the number of additional courses you take. This recommendation
may seem counterintuitive, but it has a sound basis. Right now, you need to
learn how to think for yourself. This requires active engagement, not passive
listening and regurgitation.
To learn to think, you need two things: large
blocks of time, and as much one-on-one interaction as you can get with someone
who thinks more clearly than you do.
Courses just get in the way, and if you are
well motivated, then reading and discussion is much more efficient and
broadening than lectures. It is often a good idea to get together with a few
colleagues, organize a seminar on a subject of interest, and invite a few
faculty to take part. They’ll probably be delighted. After all, it will be
interesting for them, they’ll love your initiative - and it will give them
credit for teaching a course for which they don’t have to do any work. How can
you lose?
These comments of course do not apply to
courses that teach specific skills: e.g., electron microscopy, histological
technique, scuba diving.
Write a Proposal and Get It Criticized.
A research proposal serves many functions.
1. By summarizing your year’s thinking and
reading, it ensures that you have gotten something out of it.
2. It makes it possible for you to defend your
independence by providing a concrete demonstration that you used your time
well.
3. It literally makes it possible for others
to help you. What you have in mind is too complex to be communicated verbally -
too subtle, and in too many parts. It must be put down in a well-organized,
clearly and concisely written document that can be circulated to a few good
minds. Only with a proposal before them can they give you constructive
criticism.
4. You need practice writing. We all do.
5. Having located your problem and satisfied
yourself that it is important, you will have to convince your colleagues that
you are not totally demented and, in fact, deserve support. One way to organize
a proposal to accomplish this goal is:
a. A brief statement of what you propose,
couched as a question or hypothesis.
b. Why it is important scientifically, not why
it is important to you personally, and how it fits into the broader scheme of
ideas in your field.
c. A literature review that substantiates (b).
d. Describe your problem as a series of
subproblems that can each be attacked in a series of small steps. Devise
experiments, observations or analyses that will permit you to exclude
alternatives at each stage. Line them up and start knocking them down. By
transforming the big problem into a series of smaller ones, you always know
what to do next, you lower the energy threshold to begin work, you identify the
part that will take the longest or cause the most problems, and you have available
a list of things to do when something doesn’t work out.
6. Write down a list of the major problems
that could arise and ruin the whole project. Then write down a list of
alternatives that you will do if things actually do go wrong.
7. It is not a bad idea to design two or three
projects and start them in parallel to see which one has the best practical
chance of succeeding. There could be two or three model systems that all seem
to have equally good chances on paper of providing appropriate tests for your
ideas, but in fact practical problems may exclude some of them. It is much more
efficient to discover this at the start than to design and execute two or three
projects in succession after the first fail for practical reasons.
8. Pick a date for the presentation of your
thesis and work backwards in constructing a schedule of how you are going to
use your time. You can expect a stab of terror at this point. Don’t worry - it
goes on like this for awhile, then it gradually gets worse.
9. Spend two to three weeks writing the
proposal after you’ve finished your reading, then give it to as many good
critics as you can find. Hope that their comments are tough, and respond as
constructively as you can.
10. Get at it. You already have the
introduction to your thesis written, and you have only been here 12 to 18
months.
Manage Your Advisors.
Keep your advisors aware of what you are
doing, but do not bother them. Be an interesting presence, not a pest. At least
once a year, submit a written progress report 1-2 pages long on your own
initiative. They will appreciate it and be impressed.
Anticipate and work to avoid personality
problems. If you do not get along with your professors, change advisors early
on. Be very careful about choosing your advisors in the first place. Most
important is their interest in your interests.
Types of Theses.
Never elaborate a baroque excrescence on top
of existing but shaky ideas. Go right to the foundations and test the implicit
but unexamined assumptions of an important body of work, or lay the foundations
for a new research thrust. There are, of course, other types of theses:
1. The classical thesis involves the
formulation of a deductive model that makes novel and surprising predictions
which you then test objectively and confirm under conditions unfavorable to the
hypothesis. Rarely done and highly prized.
2. A critique of the foundations of an
important body of research. Again, rare and valuable and a sure winner if
properly executed.
3. The purely theoretical thesis. This takes
courage, especially in a department loaded with bedrock empiricists, but can be
pulled off if you are genuinely good at math and logic.
4. Gather data that someone else can
synthesize. This is the worst kind of thesis, but in a pinch it will get you
through. To certain kinds of people lots of data, even if they don’t test a hypothesis,
will always be impressive. At least the results show that you worked hard, a
fact with which you can blackmail your committee into giving you the doctorate.
There are really as many kinds of theses as
their are graduate students. The four types listed serve as limiting cases of
the good, the bad, and the ugly. Doctoral work is a chance for you to try your
hand at a number of different research styles and to discover which suites you
best: theory, field work, or lab work. Ideally, you will balance all three and
become the rare person who can translate the theory for the empiricists and the
real world for the theoreticians.
Start Publishing Early.
Don’t kid yourself. You may have gotten into
this game out of your love for plants and animals, your curiosity about nature,
and your drive to know the truth, but you won’t be able to get a job and stay
in it unless you publish. You need to publish substantial articles in
internationally recognized, refereed journals. Without them, you can forget a
career in science. This sounds brutal, but there are good reasons for it, and
it can be a joyful challenge and fulfillment. Science is shared knowledge.
Until the results are effectively communicated, they in effect do not exist.
Publishing is part of the job, and until it is done, the work is not complete.
You must master the skill of writing clear, concise, well-organized scientific
papers. Here are some tips about getting into the publishing game.
1. Co-author a paper with someone who has more
experience. Approach a professor who is working on an interesting project and
offer your services in return for a junior authorship. He’ll appreciate the
help and will give you lots of good comments on the paper because his name will
be on it.
2. Do not expect your first paper to be
world-shattering. A lot of eminent people began with a minor piece of work. The
amount of information reported in the average scientific paper may be less than
you think. Work up to the major journals by publishing one or two short - but competent
- papers in less well-recognized journals. You will quickly discover that no
matter what the reputation of the journal, all editorial boards defend the
quality of their product with jealous pride - and they should!
3. If it is good enough, publish your research
proposal as a critical review paper. If it is publishable, you’ve probably
chosen the right field to work in.
4. Do not write your thesis as a monograph.
Write it as a series of publishable manuscripts, and submit them early enough
so that at least one or two chapters of your thesis can be presented as
reprints of published articles.
5. Buy and use a copy of Strunk and White’s
Elements of Style. Read it before you sit down to write your first paper, then
read it again at least once a year for the next three or four years. Day’s
book, How to Write a Scientific Paper, is also excellent.
6. Get your work reviewed before you submit it
to the journal by someone who has the time to criticize your writing as well as
your ideas and organization.
Don’t Look Down on a Master’s Thesis.
The only reason not to do a master’s is to
fulfill the generally false conceit that you’re too good for that sort of
thing. The master’s has a number of advantages.
1. It gives you a natural way of changing
schools if you want to. You can use this to broaden your background. Moreover,
your ideas on what constitutes an important problem will probably be changing
rapidly at this stage of your development. Your knowledge of who is doing what,
and where, will be expanding rapidly. If you decide to change universities,
this is the best way to do it. You leave behind people satisfied with your
performance and in a position to provide well-informed letters of
recommendation. You arrive with most of your PhD requirements satisfied.
2. You get much-needed experience in research
and writing in a context less threatening than doctoral research. You break
yourself in gradually. In research, you learn the size of a soluble problem.
People who have done master’s work usually have a much easier time with the
PhD.
3. You get a publication.
4. What’s your hurry? If you enter the job
market too quickly, you won´t be well prepared. Better to go a bit more slowly,
build up a substantial background, and present yourself a bit later as a person
with more and broader experience.
Publish Regularly, But Not Too Much.
The pressure to publish has corroded the
quality of journals and the quality of intellectual life. It is far better to
have published a few papers of high quality that are widely read than it is to
have published a long string of minor articles that are quickly forgotten. You
do have to be realistic. You will need publications to get a post-doc, and you
will need more to get a faculty position and then tenure. However, to the
extent that you can gather your work together in substantial packages of real
quality, you will be doing both yourself and your field a favor.
Most people publish only a few papers that
make any difference. Most papers are cited little or not at all. About 10% of
the articles published receive 90% of the citations. A paper that is not cited
is time and effort wasted. Go for quality, not for quantity. This will take
courage and stubbornness, but you won’t regret it. If you are publishing one or
two carefully considered, substantial papers in good, refereed journals each
year, you’re doing very well - and you’ve taken time to do the job right.
Acknowledgements
Thanks to Frank Pitelka for providing an
opportunity, to Ray Huey for being a co-conspirator and sounding board and for
providing a number of the comments presented here, to the various unknown
graduate students who kept these ideas in circulation, and to Pete Morin for
suggesting that I write them up for publication.
Some Useful References.
Day, R.A. 1983. How to write and publish a
scientific paper. 2nd ed. iSi Press, Philadephia. 181 pp. wise and witty.
Smith, R.V. 1984. Graduate research - a guide
for students in the sciences. iSi Press, Philadelphia. 182 pp. complete and
practical.
Strunk, W. Jr, and E.B. White.1979. The
elements of style. 3rd Ed. Macmillan, New York. 92 pp. the paradigm of
concision.
Stephen C. Stearns
Professor of Zoology
Zoologisches Institut der Universtät Basel
Rheinsprung 9
CH-4051 Basel, Switzerland
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