Modest Advice for Graduate Students
by Stephen C. Stearns
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
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
These comments of course do not apply to courses that teach
specific skills: e.g., electron microscopy, histological technique,
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
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
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
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
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
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
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
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
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
CH-4051 Basel, Switzerland