开学季必读 | 耶鲁大学教授给研究生们11条建议
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来源 / 搜狐网
Stephen C. Stearns / 耶鲁大学教授
永远要做好最坏的打算
凡事预则立，不预则废。你只要做一点点的“预”，就可以让你在博士生涯中避免一些灭顶之灾。想吐槽就吐槽吧（Be cynical）。假如你的研究计划行不通，假如某个导师非但对你的研究计划不予支持，甚至嗤之以鼻。那么，你还是赶紧换一个研究题目为妙。
别指望教授来管你
现实中，有些教授会去管你，有些则不会去管你。大部分教授估计想管你，但他们整日都忙得晕头转向，不亦乐乎，自己都顾不过来，那有时间去管你呢，爱莫能助。那么，你就得完全靠自己，而且最好习以为常。我这么说有多层含义，其中两个要点是：
1. 你最好尽早确定你到底想做什么题目。
学位是你要去拿，而不是教授要去拿，你要你自己去争取。当然，导师也不会袖手旁观，导师会给你一些指导，也会在一定程度上帮你解决你在培养程序和经费上的后顾之忧，但是，且记：导师不会手把手地告诉你你的论文如何做。很多事情都取决于你自己。如果你需要导师指导，你就去问导师；这是他义不容辞的责任。
2. 如果你想得到别人的指导，那你就必须主动地找他/她，别守株待兔。
你必须知道你的研究工作的重要性之所在
当你初来咋到，你得在第一年广泛地阅读和思考。学而不思则罔，思而不学则殆。可能会出现这样的情况：你感觉你阅读的那些文献，都完全没用，后来你会品味出原来不是那样。如果文献中有些东西你看不懂，不要灰心丧气，可能那不是你的问题，而是作者的问题，他／她可能根本就没有说清楚。
如果某个大权威对你说，你将一无所获，原因是你没有去上课，没有获得数据，那么，请你勇敢地告诉他／她，你会出成果的。如果他们依旧固执己见，那就跟他／她拜拜。唯有你自己最清楚自己工作的意义，让他见鬼去吧。
这个阶段会让人有受煎熬、受挫折的感觉，为伊消得人憔悴。但天无绝人之路。你需要冷静地思考，不断问问自己：我现在在这里究竟在干啥？要沉得住气。这个阶段对你的个人生涯发展至关重要，同时对出新思想至关重要。
此时，你得考虑，究竟什么东西可以构成一个重要的科学问题。这个决定必须由你自己独立做出，理由有二：
首先，如果你研究的问题是别人给你的，你会感到这个问题是别人要你去做，而不是自己要去做，因而不会捍卫它，不会为之奋斗，直至获得漂亮的结果。
第二，你攻读博士学位期间的研究工作，会影响你未来的发展。你未来将献身于哪个领域，这个决定必须由你自己自主的作出。
慎重地选择你的科研方向，这对科学的发展也是非常重要的。也许在这个方向上你可以开辟一个全新的天地。请记住：如果你根本不知道为什么要做某个研究，就去开始去收集数据，那有什么意义呢？那是做无用功。
要克服心理障碍
在你的研究生生涯早期，你就必须培养坚忍不拔的心理素质，这样就不至于被后来可能碰到的各种挫折所干扰。如果你不时刻保持警惕，那么课业的压力、听课的压力、语言的压力以及其他种种意料之外的压力，会把你忙得团团转，像一个无头苍蝇一样儿，或者说像一个分子做杂乱无章的布朗运动。以下列举一些注意事项：
1.仔细斟酌博士选题，并为之奋斗终身。
无论你多么努力，你都将无法规避你的课题问题。每人都如此，这源于论文的开放性。你必须学会判断什么样的论文是“好”论文。和世界上其他事物一样，你得意识到不可能有“完美”的论文的存在。静下心来，在有限时间、金钱、精力、激励和思考下，尽你所能，把论文修改到最好。
在研究生涯的早期，你可以通过完成所有既定的任务来减缓论文的问题。所以请尽早修完你的所有课程并完成相应的考试。这不仅清除了准备学位论文前的障碍，在成功完成这些任务后，你可能足够出色了。
2. 唯马首是瞻的行为不会有出色的表现，建议你与同实验者以同事的关系相处。
论文是你不得不面对的硬指标，而同事或者合作者的态度则是一个不明的挑战。如果你表现得像一个同事，别人也会把你看成是一个同事。
读研究生只是改变你的未来发展的途径之一。如果出现了更好的机会，那就不妨做一个“逃兵”。有三个好理由值得这样做：
首先，可能这真的是个好机会，而且这个机会比读研究生所做的任何事都更有创造性和挑战性。当你有足够长时间来证明辍学是一个不错的选择时，那就暂时放弃读研吧。比如一个跟你研究工作不是直接相关的非洲野外项目、一个软件开发的合同、一个在首府科技政策制定部门当助手的工作机会，或者在某个主流报纸/杂志社当科学栏目实习记者的机会。
其次，只有当你在关注这种机会时，你才能被称为是一个真正独立的研究生。如果你认为读研究生是你唯一的选择，你会于心不安，容易变得有些沮丧并且心态不稳，当然没法回到最佳状态。
最后，如果读研真的不合适你，强扭的瓜也不甜，您甚至会因此失去更多其他的机会。除了当一位科学家，生活中还有许多其他有趣的事情值得去做，也许人力市场找到的一些工作比当科学家好得多。如果你真的不适合当科学家，或许你应该尝试其他的工作。
但是，千万不要鲁莽行事，这是一个很严肃的决定。在做出最后决定前，应该和研究生院的负责人以及人品不错的老师谈谈想法，他们会给你不错的建议。
尽量少选课，多阅读多讨论
如果你对你的研究领域已经相当熟悉，那么就尽量减少上课的数量。这个建议看上去和之前有点自相矛盾，其实有它的道理。当下，你应该学会如何为你的课题思考。这需要你主动出击，而不是被动地听课和机械地重复。
学会思考，你需要两样东西：一是得有大块完整的时间；其次是，和那些对科学问题理解得更透彻的人进行一对一的交流。
过多的上课可能适得其反。如果你很有积极性，那么阅读和讨论将会比听课更有效、更具有启发性。通常我会建议，跟少数几个同事组织一个大家都感兴趣的课题，并邀请一两位老师参加。老师们一般都会很乐意参加，因为他们对讨论的课题也很感兴趣，也会喜欢你们的创意。这种讨论会，同时将给该科目的老师积累一定的信誉，关键是他们还不用做任何工作。何乐而不为呢？
当然，这些建议不适用于一些介绍专业技能的课程，比如电镜成像、组织学和轻潜水技术等等。
写研究计划，并征求别人的意见
撰写研究计划有许多好处：
1. 总结一年来你所看和所想的内容，并通过梳理与总结，激发你的新想法。
2. 通过提供一个具体的演示来证明你在合理地利用时间，并以此来维持做事的独立性。
3. 互利互惠。没经过梳理的口头交流太零碎，而经过细心整理的文档能在同行之间传阅，并获得他人的意见，旁人只有在阅读了你的研究计划以后才可能给出一些建设性的意见。
4. 你需要学习如何写文章，我们也一样。
5. 找到让你自己满意的科学问题，这一点很重要的。你需要向同事证明你并不是完全对此手足无措，并且得到大家的支持。
提出一个研究计划，并达成这个目标的方法是：
1. 一份有关你的研究计划的简短陈述，这是一个科学问题或者假说。
2. 从学术角度，而不是从你个人的角度，提出该假说的重要性，以及该假说如何与你所研究的其他领域内的想法相结合。
3. 用详尽的文献综述来证实你所提到的有关该假说的重要性。
4. 把你的科学问题拆分成若个小问题，并逐个击破。
在设计实验、观察以及分析时，请确保在每一阶段都准备好备选实验。把这些步骤一个个罗列起来，并逐个解决这些问题。通过把大问题转化成一系列的小问题，你可以永远知道下一步该怎么做，以此减轻刚开始面对一个大问题时的手足无措。你可以从中知道哪些问题、哪些步骤比较费时，或者困难比较大，来列出各个事情的优先顺序。当你明白一些步骤没法解决时，你有其他一系列的事情可以做。
5. 写出一系列可能出现并对整个项目具有毁灭性打击的大问题，并按此写出的相应的备选实验，以防所担心的问题在实验中真的出现。
6. 设计两到三个实验并同时开展，以此确定哪个实验最可能成功，这或许是个不错的主意。
这可能同时有两到三个模型对你的想法有相似的解释力度，但是在实际操作中，可能不得不面临这些问题。刚开始就发现这些问题，比在同时开展两到三个实验，并当第一个实验失败后再考虑这些问题更有效。
7. 给你的论文报告选定一个日期，并合理安排报告开始前的这段时间。
给自己设定好截止日期后，你会有紧张感。别担心，当这样进行一段时日后，这种紧张感会更加强。
8. 在你完成文献的阅读之后，需要花费两到三周的时间来撰写研究计划，并争取给更多的同行评阅，以此得到尽量多的评审意见。希望他们返回的意见是有所帮助，然后你再针对这些意见逐一回复。
9. 当完成这些步骤都时，你其实已经差不多写好了引言部分了，这将花费你一到一年半的时间。
时不时向导师汇报进展
让你的导师时刻知道你在做什么，但不要打扰到他(们)，让导师们对你的出现感兴趣，而不是像对待害虫一样。每年至少主动提交一份一至两页纸的研究进展报告，他们会欣赏你这样的举动，并会对此留下良好印象。
预见并尽量避免跟导师出现个人争端。如果你跟你的导师难以继续相处，那么趁早换导师吧。刚开始选择导师需要非常谨慎，其中最重要的一点是：你跟导师的研究兴趣需要保持一致。
了解不同类型的论文
千万不要在已有的但不确定的想法上说一大堆华而不实的废话。直入主题，并验证一些重要环节中具有主要研究意义但未曾检验的假说，或者列出一个新研究的提纲。当然，这里还有其他类型的论文：
1. 经典的论文包括模型的演绎推算。
这些模型会相当新颖，并得到令人惊奇的预测，在此之后你得在对该假说不利的情况下，客观地验证并证实它。这是事半功倍的做法。
2. 对现有的某个重要研究理论进行批评。
同样，如果能够合理解释，你也能成为少数几个令人尊敬的赢家。
3. 纯理论研究的论文。
这需要勇气，尤其是在一个经验主义者占主导的研究领域，但是如果你在数学以及推理能力上足够强的话，你也会成功。
4. 收集一些别人也同样能收集的数据，这是最糟糕的论文，但是有时候可以帮你突围。
对于一部分拥有一大堆数据的人，那怕他没有验证一个假说，有时也会给人留下深刻印象。至少结果说明你已经努力工作了，你可以因此向你的评审委员会索求授予你博士学位。
论文的类型其实相当多，就跟有多种研究生一样。之前所列举的四种论文分别提供了好、差以及糟糕论文案例。博士论文的研究工作提供了让你尝试各种研究类型的机会，并让你发现哪种研究最适合你：理论研究、野外工作还是实验室工作？理想状况下，你能权衡三者，成为凤毛麟角的集大成者：从经验主义者的角度思考理论问题，从理论学家的视角解决现实世界的问题。
趁早发文章
别骗自己了，当你进入这个发表论文的节奏当中时，你得暂时远离你所钟爱的动植物、所好奇的大自然及探索真理的热情。因为如果你没有发表论文，你将找不到一份长期的工作；如果你真的没有论文好发表，你倒真可以放弃科研这条路了。
这听上去很残忍，但也有它的道理。实际上，发表论文是一个很有趣的挑战和实现理想的过程。科学是共享的，在科研结果无法得到有效地交流之前，其实它们并不存在。发表论文只是科研工作的一部分，直到文章发表，才意味着该研究工作的结束。你必须掌握撰写简洁扼要，高质量的学术论文的技能。以下是几点有关发表论文的提示：
1. 跟一些更富论文撰写经验的人共同发表论文。
跟当下有共同研究兴趣的教授套近乎，如果他愿意，他会给你的论文发表有所助益。作为回馈，将他署名为论文的主要合作者，他将会很感激，并给你的论文提供许多好的修改建议。
2. 别期望你的第一篇论文就能举世震惊。
许多杰出的科学家都是从很小的研究工作开始的。学术论文所报道的平均信息量可能比你想像的要少，先在一些不太出名的期刊上发表一到两篇完整的论文，再在之后把目标定向主流杂志。不久你就会发现，不管杂志的名声如何，所有杂志编委都会竭尽全力来保证所任杂志发表论文的质量－这也正是他们的职责！
3. 如果你的研究计划已经足够完美，那么可以把它以评论性的综述论文来发表。如果论文发表了，你可能已经选择了合适的研究领域，并可以对此继续开展研究。
4. 不要把你的博士论文写成“教科书”。
可以把你的博士论文写成一系列可以发表的稿件，然后尽早把它们投出去，因此在答辩前，至少博士论文中的一到两章可以成为在刊或刊出的文章。
5. 购买一本William Strunk和E. P. White合著的“Elements of Style”。
在你准备开始撰写第一篇论文之前，请仔细阅读此书，然后每隔三四年至少再阅读一遍。Robert Day的“How to Write a Scientific Paper”这本书也不错。
6. 在你投稿之前，让一个有时间能够对你论文的写作、想法和条理性提出修改意见的人修改。
可别小看硕士论文
不读硕士的唯一理由常常成为一个普遍的误区：我已经足够好了，没必要做类似硕士论文的事情。其实，完成硕士论文有许多好处：
读硕士，你有一个换学校的机会。你可以利用这一点拓宽你的研究背景。此外，在你当下的发展期，有关你对“一个重要问题由哪些部分组成”的想法可能会迅速转变。你会迅速了解更多学者所做的研究，以及他们各自开展研究的地点。如果你打算换学校，读硕士是最好的方式。你离开母校，母校的同行对你的表现也挺满意，并且他们给你提供了一份很给力的推荐信。此时，你已经满意地达到了攻读博士的要求。
你积累了许多科学研究中急需的经验，并且在比博士研究风险更小的环境下撰写论文。你可以逐渐挑战你自己。在研究中，你见识了解决一个科学问题的难易程度。经历过硕士阶段的人们常常会更加容易地完成博士论文的研究工作。
你有在硕士期间发表的论文。
你急啥呢？如果你过早地开始找工作，你可能还没有完全准备妥当。最好稍微晚点出手，先逐渐加强你的背景基础，然后再展现拥有更多和更广经验的你。
定期发表高质量的论文
发表论文的压力已经侵蚀了杂志的质量，并同时也侵蚀了作者的精神生活。发表几篇能够被广为阅读的高质量论文会比发表一些列迅速被人遗忘的小文章要好很多。
你也得回到现实，你需要发表论文来获得博士后岗位，并发表更多的论文来获得一个教职，直至获得终身教职。但是，如果你能把你的研究工作持续发表成连续的高质量论文，那么无论对于你个人，还是你所研究的学科，都是极好的事情。
大多数人只发表少量能够引起重大影响的文章。大多数文章的被引用数会很少，甚至没有被引用。要知道，90％的引用是约10％的论文贡献的。没有被引用的文章是时间和精力的浪费。追求高质量，而不是数量，这需要勇气和毅力，但是你不会因此后悔。如果你能够发表一至两篇精雕细琢有明显突破的好文章，并且每年被持续引用，那么表明你将会做得很出色，也表明你已经把时间花在刀刃上了。
原文如下：
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.
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