[转载]Some useful tools for graduate school success

无意间发现的一个在线资源,读完了非常鼓舞,值得订阅。

http://gradlogic.org/category/interview/

  1. Follow your passions and talents 
  2. Pick your advisor and lab wisely [可以好好看看在调研导师的时候需要注意的问题]
  3. Learn to write well
  4. Get confused. Try new things. Risk failure.

外加一个有趣的个人职业发展评估工具:The MyIDP tool can help you identify your strengths.

Be very selective and deliberate when you decide how to spend your time: Your Bag of Apples | Set Realistic Goals.

Creating a To Be list can help you to preserve the essence of yourself.

 

 

 

Research Methodology | Manove’s Dissertation Advice for PhD Students

Manove’s Dissertation Advice for PhD Students

In my first year at college, I was assigned an adviser from the physics department.  He was a senior professor, not too many years from retirement.  “You can ask me anything you want,” he said in our first meeting, “but don’t ask me about sex—I don’t remember it.”  I finished my own thesis more than 40 years ago, so perhaps I ought to adopt a similar attitude about dissertations.  Instead, I will bother you with unsolicited advice.  My advice is completely unofficial: it does NOT represent department policy in any way.

When to Get Started

“Anyone can write a good dissertation,” they say, “but not everyone can finish it quickly.”  Yes, but it helps if you get an early start.  If you want, you can sit around thinking, “I don’t have any ideas,” “I’m embarrassed to talk with a professor,” or  “I have to put all of my energy into being a TA.”  Those feelings are natural, but it’s in your self-interest to ignore them.  Some students say to themselves, “Now that I’ve finished my coursework, I’ll relax for a year.” Sure, you deserve a rest, but the opportunity cost of a long rest is certain to be very high.  In my view, you should start working on your thesis as soon as your second-year paper is finished and you have no more than one course left to complete.  Normally, this means that you should start working on your dissertation by the end of the first semester of your third year, or sooner.

Choosing a TopicMichelangelo

Michelangelo wrote: “Every block of stone has a statue inside it, and it is the task of the sculptor to discover it.”  Likewise, after years of coursework, after reading the newspapers, after listening to professors, preachers and politicians, you have a good idea for a dissertation topic somewhere inside your brain.  You have only to find it.  And a topic that you discover yourself is bound to be more motivating than one suggested by an adviser would be.  Almost everything that goes on in this world, from sinning to soccer, has an economic aspect that can be explored.  Inasmuch as pure theory and econometric theory aren’t exactly about what goes on in the world, the discussion below is probably less applicable to those fields.

Unless you are a true genius, a good thesis topic is a narrow topic, not one designed to revamp a field of economics.  But narrow topics can help answer broad questions.  Last week [5/11/2011] , Phil Oreopoulis presented a lecture entitled, “What Does Schooling Do?”  A lot of work has been done on in this area, but little is known.  Do students learn productive skills in their coursework? Or do they merely learn self-discipline and how to meet deadlines?  Does schooling yield positive externalities to others in the community?  Do people attend college as a signal of their ability?  Or is college primarily a consumption activity?  There’s room for a thousand new papers here alone.

To me, the most important question in development economics is “Why are poor countries poor?”  There must be a large number of partial answers to that question.  Can you find one of them?  Or why is China getting rich so fast?  If you’ve lived in China, you may have a small idea that you can develop in this area.

Of course, if you like the idea in your second-year paper, you may want to continue to work on that topic.  If you’re bored with it, choose something else.  It’s hard to work when you are bored.

The department has many research seminars and workshops, some say too many.  Check them out athttp://www.bu.edu/econ/events/.  Start attending them in your second year, and by your third year, try to attend at least two a week.  In many of the workshops, PhD students are presenting their research.  These are great places to see what others are doing and to help you find ideas for your own research.

Keep in mind that “the best is an enemy of the good.”  You don’t need a formal search model to know that it doesn’t make sense to search until you find the perfect topic.  Start working on something quickly; you’ll have plenty of time to shift the topic as you go.  After you find an idea of interest, write up a description of the idea in a few pages of prose—no math or econometrics allowed.  Then go off to talk with faculty members.  [Caution: some pure economic and econometric theorists dislike the verbal approach, but I myself believe in it.]

Finding Dissertation Advisers

All faculty members are busy.  Some are busy working, and some are busy feeling guilty about not working enough.  But that’s their problem, not yours.  Your problem is to find several faculty members (normally three), busy or not, who can advise you on your dissertation.  When you want to meet with a faculty member, send an email asking for an appointment.  If she doesn’t answer within a day or two, just resend the email (no need to write another one).  If the faculty member says, “I don’t have much time this week,” you can respond, “When will you have time?”  Eventually, you will have an appointment.

Begin discussing your ideas with faculty as soon as you have written a few pages describing one or more of your ideas.  This should happen by the end of the first semester of your third year.  Talking with a person of the opposite sex (or the same sex if you prefer) doesn’t require you to marry him or her.  Likewise, talking with a faculty member about a research idea, doesn’t require you to adopt her as an adviser.  That can come later, after you have been meeting with the person on a regular basis.  Meet with several faculty members.  If you are working on health economics, for example, you may want to meet with someone who is knowledgeable about the institutions in your favorite country, someone else who knows theory, and someone else who has experience with empirical work and data (yuk).  If you enter a faculty member’s office, and find it too messy or too clean, or if his shirt is the wrong shade of pink, then try someone else.  Shop around.

Some faculty members already have a large number of advisees, and some, especially the younger set, may have very few.  You can find out how many by asking around or by asking Andy Campolieto, who tends to know these things.  As with most choices, there’s a tradeoff here.  Having lots of advisees is a good signal about advising quality, but it may be a bad signal about available time.  Younger faculty with few advisees may be able to give you more time, may have lots of fresh ideas, and may have very up-to-date knowledge of technical tools.  Take a look at their CVs to see what they are publishing.  And don’t forget that if you want to be a professor when you grow up, you might look for a primary adviser (first reader) who has lots of contacts and can help you get a good academic job.

Try to see your advisers on a regular basis, at least every week or two.  The main reason for doing this is not to hear their penetrating comments, but rather to keep yourself working.  It’s embarrassing to return to a professor’s office and say, “I haven’t done any research in the last two weeks.”  You will have a strong incentive to work hard and avoid embarrassment, which is the most painful and best remembered of all emotions.

If you plan to write an empirical thesis, and most of you should, you will need data.  The most important thing you need to know about data is that the word “data” is plural.  If you accidentally say “this data” instead of “these data” you won’t sound like the pompous scholar that you want to be.  The next most important thing to know about data is what data to get and how to get them.  Good advisers can be especially helpful for this, though some of you may have special knowledge or connections with institutions in your home country that will permit you to acquire data on your own.  In any event, you should start working on data acquisition as early as possible, because the process can be slow and sometimes costly.  You may also have to clean the data before you use them, an activity that requires both the innocence of youth and the guiding hand of an adviser who wouldn’t want to do it herself.

The Dissertation Proposal

In recent years the dissertation proposal has become nothing more than a rehearsal for the dissertation defense, a situation that leaves the proposal almost useless.  But now the GIC is attempting to turn back the clock and turn the “proposal” back into a proposal, i.e., a proposed plan for the research to come.  In his recent statement on procedures for PhD dissertations, Bart Lipman states that the proposal “needs to be specific enough that your advisors [he means “advisers”] can say with a reasonable degree of confidence that at least most of what you propose to do can be done and is worth doing.”  I would say it this way: the plan of research described in your proposal should be feasible and sufficient to qualify you for the degree.  I recommend that you include a detailed table of contents in the proposal, and next to each item write “completed” if it has been completed or the date by which you plan to complete it.  If your committee accepts your proposal, it serves not only as a research plan, but also as an informal contract that sets out what you are expected to do in the final dissertation.  If you do what you say you will in the accepted proposal, your advisers are less likely to insist on more work later.

The GIC has decided to impose a deadline for the proposal at the end of May of your fourth year.  I think that their deadline is far too late.  If you begin working on your dissertation in the first semester of your third year, as you should, then May of your fourth year will seem very far away.  You may be seduced into spending all your time teaching, talking with your mom on the phone, or worrying about your kids, none of which are productive activities.  Find a commitment device that requires you to defend your proposal during the first semester of your fourth year.  For example, you could give $1000 to Albert Ma, and tell him that he can keep $20 for each day that you are late.  If you miss the early deadline, it will be a lot less painful than losing your financial aid in the fifth year, which is what happens if your proposal is not successfully defended by the May-31 deadline set by the GIC.

The Job-Market Paper

If you want to obtain a good research-oriented job, you will need to complete a potentially publishable job-market paper by the end of October in the year you go on the market, normally your fifth year.  The October deadline is not a flexible one: every day that goes by after that deadline lowers your expected number of interviews at the Meetings.  Without interviews you won’t have fly-outs, and no fly-outs, no-job.  Yes, there are exceptions, and the Catholic Church recognizes miracles, but these are rare.

The job-market paper is usually a completed chapter of the doctoral dissertation.  If you defend your proposal at the end of May, you will have five months to complete the paper, which isn’t a lot of time to get your first publishable paper ready.  That’s another reason why I recommend an earlier December deadline for the proposal.

I’ve started to read many job-market papers, and I’ve read a few of them completely.  The most important thing about a job-market paper (or any research paper) is the title.  A good title is informative, though probably not cute.  If the title sounds uninteresting, a potential reader is likely to move on to the title of someone else’s paper.  Next comes the abstract.  The abstract should explain in a few words what you have done and why it’s important or even surprising.  If the abstract is dull or incomprehensible, the reader is likely to assume that the rest of the paper is the same way and place it gently into the recycle bin.  (This is a bad thing, because recycled paper lowers the demand for wood pulp and reduces the incentive to grow trees.)  Next in importance comes the introduction.  Here you not only explain what you’ve done and why it’s important, but you also explain the intuition behind your idea in words.  Provide examples wherever possible.  If after reading the introduction, I don’t understand what the author is doing, I assume (correctly) that the author doesn’t understand what he is doing either, and I go no further.

As for the rest of the paper, you want to continue to emphasize intuition and examples.  Put most of the nasty math and proofs of propositions in the appendix.  Some economists think that lots of technical stuff will impress others in the profession.  But the truth is that too much math interrupts the flow of your argument.  In fact, very few economists like to read math, and those who do are likely to be rather strange—just think about my colleagues in theory.  Be sure to finish your paper on time, be sure that your advisers read the paper and quiz you about it, and have it copyedited before you send it out.

The Doctoral Dissertation

The normal dissertation consists of three papers, related or otherwise.  Two of the papers should be pretty good, and potentially publishable; the third paper can be a kind of filler so long as it doesn’t embarrass you or the department.  The entire dissertation has a title and an abstract, which the dean reads (make sure it’s grammatical), and, normally, an introduction and conclusion.  The thesis as a package isn’t very important nowadays—nobody but your mother or father is likely to pay any attention to it.  It’s the papers inside the thesis that are of interest: you will put them online and eventually submit them for publication.

The Dissertation Defense

Before you can graduate with your PhD, you must describe your dissertation in a so-called dissertation defense.  At BU (and in most US universities) the defense is an informal formality that takes place when the dissertation is substantially complete.  You will have about an hour to review your work and answer questions from the examining committee.  After that, the examining committee meets and decides whether or not you passed the defense (almost everyone does) and then decides whether or not a bit more work is necessary (it usually is).

The examining committee consists of five people: your three advisers and two other faculty members who serve as warm bodies.  Your advisers are expected to read and comment on various versions of your thesis in advance of the defense; the warm bodies (fourth reader and chair of the examining committee) are expected to attend the defense and ask a question or two during your presentation.  With the agreement of the DGI, you may be able to choose the warm bodies yourself, but be careful: they must be intelligent enough to write their initials on the required form and to sip the cheap champagne-like fluid they serve after they tell you that you’ve passed.  I myself often serve as a warm body, and I enjoy the process.

Conclusion

The main ingredients for success in a PhD program are self-confidence, self-discipline and ambition.  Intelligence has little to do with the process.  I’m confident that I’ve given you good advice, even though some of my colleagues will undoubtedly think it’s disastrous.  Fortunately, by the time you find out and decide to hold me responsible, I probably will have retired and gone off to enjoy the sunshine in Tenerife or some such place.  This is odd, because I don’t like sunshine.

Research Methodology | Some Cynical Advice for Graduate Students

数年前,标题中还是cynical,现在已然改成了Modest.在北大曾经与Dr. Stearns 有过一面之缘,说实话,还是cynical更适合他。非常好的学术研究建议,其中描写的pitfall我几乎条条必中,深为惭愧。对于一个追求自我成长的研究者来说,应该时时参照,反思调整。

Biography

Prof. Stearns specializes in life history evolution, which links the fields of ecology and evolutionary biology, and in evolutionary medicine. He came to Yale in 2000 from the University of Basel, Switzerland, where he had been professor of zoology since 1983 and held several administrative posts.

His books include “Evolution, an introduction” (Oxford, 2000, 2nd Ed 2005) with Rolf Hoekstra, “Watching, from the Edge of Extinction” (Yale, 1999) with his wife Beverly Peterson Stearns, “The Evolution of Life Histories” (Oxford, 1992), and two edited volumes, “Evolution in health and disease” (Oxford, 1998, 2nd Ed 2008) and “The Evolution of Sex and its Consequences.”

A 1967 graduate of Yale College, Stearns earned a M.S. from the University of Wisconsin and a Ph.D. from the University of British Columbia.  He was a Miller Fellow at the University of California, Berkeley, before taking up an appointment at Reed College prior to moving to Switzerland.

Prof. Stearns founded and has served as president of both the European Society for Evolutionary Biology and the Tropical Biology Association and was founding editor of the Journal of Evolutionary Biology. He has been a vice president of the Society for the Study of Evolution and is a fellow of the American Association for the Advancement of Science.

—– cite from:  http://stearnslab.yale.edu/some-modest-advice-graduate-students —————–

Some Modest Advice for Graduate Students

Some 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 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