今天才看到Michael Atiyah的这篇文章。同时听了他的原版Talk的录像。最后有学生提问部分这里没有。有一个学生问：您如何精通这么多方向？答曰：向这方向一流人士请教。得到最高级的思想，以后补充很快。不要请教二流。。。。。。下面原文： Warning What follows is very much a personal view based on my own experience and reflecting my personality, the type of mathematics that I work on, and my style of work. However, mathematicians vary widely in all these characteristics and you should follow your own instinct. You may learn from others but interpret what you learn in your own way. Originality comes by breaking away, in some respects, from the practice of the past. Motivation A research mathematician, like a creative artist, has to be passionately interested in the subject and fully dedicated to it. Without strong internal motivation you cannot succeed, but if you enjoy mathematics the satisfaction you can get from solving hard problems is immense. The first year or two of research is the most difficult. There is so much to learn. One struggles unsuccessfully with small problems and one has serious doubts about one’s ability to prove anything interesting. I went through such a period in my second year of research, and Jean-Pierre Serre, perhaps the outstanding mathematician of my generation, told me that he too had contemplated giving up at one stage. Only the mediocre are supremely confident of their ability. The better you are, the higher the standards you set yourself—you can see beyond your immediate reach. Many would-be mathematicians also have talents and interests in other directions and they may have a difficult choice to make between embarking on a mathematical career and pursuing something else. The great Gauss is reputed to have wavered between mathematics and philology, Pascal deserted mathematics at an early age for theology, while Descartes and Leibniz are also famous as philosophers. Some mathematicians move into physics (e.g., Freeman Dyson) while others (e.g., Harish Chandra, Raoul Bott) have moved the other way. You should not regard mathematics as a closed world, and the interaction between mathematics and other disciplines is healthy both for the individual and for society. Psychology Because of the intense mental concentration required in mathematics, psychological pressures can be considerable, even when things are going well. Depending on your personality this may be a major or only a minor problem, but one can take steps to reduce the tension. Interaction with fellow students—attending lectures, seminars, and conferences—both widens one’s horizons and provides important social support. Too much isolation and introspection can be dangerous and time spent in apparently idle conversation is not really wasted. Collaboration, initially with fellow students or one’s supervisor, has many benefits and long-term collaboration with coworkers can be extremely fruitful both in mathematical terms and at the personal level. There is always the need for hard quiet thought on one’s own, but this can be enhanced and balanced by discussion and exchange of ideas with friends. Problems versus Theory Mathematicians are sometimes categorized as either “problem solvers” or “theorists.” It is certainly true that there are extreme cases that highlight this division (Erd˝os versus Grothendieck, for example) but most mathematicians lie somewhere in between, with their work involving both the solution of problems and the development of some theory. In fact, a theory that does not lead to the solution of concrete and interesting problems is not worth having. Conversely, any really deep problem tends to stimulate the development of theory for its solution (Fermat’s Last Theorem being a classic example). What bearing does this have on a beginning student? Although one has to read books and papers and absorb general concepts and techniques (theory), realistically, a student has to focus on one or more specific problems. This provides something to chew on and to test one’s mettle. A definite problem, which one struggles with and understands in detail, is also an invaluable benchmark against which to measure the utility and strength of available theories. 1 2 Princeton Companion to Mathematics Proof Depending on how the research goes, the eventual PhD thesis may strip away most of the theory and focus only on the essential problem, or else it may describe a wider scenario into which the problem naturally fits. The Role of Curiosity The driving force in research is curiosity. When is a particular result true? Is that the best proof, or is there a more natural or elegant one? What is the most general context in which the result holds? If you keep asking yourself such questions when reading a paper or listening to a lecture, then sooner or later a glimmer of an answer will emerge—some possible route to investigate. When this happens to me I always take time out to pursue the idea to see where it leads or whether it will stand up to scrutiny. Nine times out of ten it turns out to be a blind alley, but occasionally one strikes gold. The difficulty is in knowing when an idea that is initially promising is in fact going nowhere. At this stage one has to cut one’s losses and return to the main road. Often the decision is not clear-cut and in fact I frequently return to a previously discarded idea and give it another try. Ironically, good ideas can emerge unexpectedly from a bad lecture or seminar. I often find myself listening to a lecture where the result is beautiful and the proof ugly and complicated. Instead of trying to follow a messy proof on the blackboard, I spend the rest of the hour thinking about producing a more elegant proof. Usually, but not always, without success, but even then my time is better spent, since I have thought hard about the problem in my own way. This is much better than passively following another person’s reasoning. Examples If you are, like me, someone who prefers large vistas and powerful theories (I was influenced but not converted by Grothendieck) then it is essential to be able to test general results by applying them to simple examples. Over the years I have built up a large array of such examples, drawn from a variety of fields. These are examples where one can do concrete calculations, sometimes with elaborate formulas, that help to make the general theory understandable. They keep your feet on the ground. Interestingly enough, Grothendieck eschewed examples, but fortunately he was in close touch with Serre who was able to rectify this omission. There is no clear-cut distinction between example and theory. Many of my favourite examples come from my early training in classical projective geometry: the twisted cubic, the quadric surface, or the Klein representation of lines in 3-space. Nothing could be more concrete or classical and all can be looked at algebraically or geometrically, but each illustrates and is the first case in a large class of examples which then become a theory: the theory of rational curves, of homogeneous spaces, or of Grassmannians. Another aspect of examples is that they can lead off in different directions. One example can generalize in several different ways or illustrate several different principles. For instance, the classical conic is a rational curve, a quadric, and a Grassmannian all in one. But most of all a good example is a thing of beauty. It shines and convinces. It gives insight and understanding. It provides the bedrock of belief. Proof We are all taught that “proof” is the central feature of mathematics, that Euclidean geometry with its careful array of axioms and propositions has provided the essential framework for modern thought since the Renaissance. Mathematicians pride themselves on absolute certainty, in comparison with the tentative steps of natural scientists, let alone the woolly thinking of other areas. It is true that, since G¨odel, absolute certainty has been undermined, and the more mundane assault of computer proofs of interminable length has induced some humility. Despite all this, proof retains its cardinal role in mathematics and a serious gap in your argument will lead to your paper being rejected. However, it is a mistake to identify research in mathematics with the process of producing proofs. In fact, one could say that all the really creative aspects of mathematical research precede the proof stage. To take the metaphor of the “stage” further, you have to start with the idea, develop the plot, write the dialogue, and provide the theatrical instructions. The actual production can be viewed as the “proof”: the implementation of an idea. In mathematics, ideas and concepts come first, then come questions and problems. At this stage the search Princeton Companion to Mathematics Proof 3 for solutions begins, one looks for a method or strategy. Once you have convinced yourself that the problem has been well-posed, and that you have the right tools for the job, you then begin to think hard about the technicalities of the proof. Before long you may realize, perhaps by finding counterexamples, that the problem was incorrectly formulated. Sometimes there is a gap between the initial intuitive idea and its formalization. You left out some hidden assumption, you overlooked some technical detail, you tried to be too general. You then have to go back and refine your formalization of the problem. It would be an unfair exaggeration to say that mathematicians rig their questions so that they can answer them, but there is undoubtedly a grain of truth in the statement. The art in good mathematics, and mathematics is an art, is to identify and tackle problems that are both interesting and solvable. Proof is the end product of a long interaction between creative imagination and critical reasoning. Without proof the program remains incomplete, but without the imaginative input it never gets started. One can see here an analogy with the work of the creative artist in other fields: writer, painter, composer, or architect. The vision comes first, it develops into an idea that gets tentatively sketched out, and finally comes the long technical process of erecting the work of art. But the technique and the vision have to remain in touch, each modifying the other according to its own rules. Strategy In the previous section I discussed the philosophy of proof and its role in the whole creative process. Now let me turn to the most down-to-earth question of interest to the young practitioner. What strategy should one adopt? How do you actually go about finding a proof? This question makes little sense in the abstract. As I explained in the previous section a good problem always has antecedents: it arises from some background, it has roots. You have to understand these roots in order to make progress. That is why it is always better to find your own problem, asking your own questions, rather than getting it on a plate from your supervisor. If you know where a problem comes from, why the question has been asked, then you are half way towards its solution. In fact, asking the right question is often as difficult as solving it. Finding the right context is an essential first step. So, in brief, you need to have a good knowledge of the history of the problem. You should know what sort of methods have worked with similar problems and what their limitations are. It is a good idea to start thinking hard about a problem as soon as you have fully absorbed it. To get to grips with it, there is no substitute for a handson approach. You should investigate special cases and try to identify where the essential difficulty lies. The more you know about the background and previous methods, the more techniques and tricks you can try. On the other hand, ignorance is sometimes bliss. J. E. Littlewood is reported to have set each of his research students to work on a disguised version of the Riemann hypothesis, letting them know what he had done only after six months. He argued that the student would not have the confidence to attack such a famous problem directly, but might make progress if not told of the fame of his opponent! The policy may not have led to a proof of the Riemann hypothesis, but it certainly led to resilient and battle-hardened students. My own approach has been to try to avoid the direct onslaught and look for indirect approaches. This involves connecting your problem with ideas and techniques from different fields that may shed unexpected light on it. If this strategy succeeds, it can lead to a beautiful and simple proof, which also “explains” why something is true. In fact, I believe the search for an explanation, for understanding, is what we should really be aiming for. Proof is simply part of that process, and sometimes its consequence. As part of the search for new methods it is a good idea to broaden your horizons. Talking to people will extend your general education and will sometimes introduce you to new ideas and techniques. Very occasionally you may get a productive idea for your own research or even for a new direction. If you need to learn a new subject, consult the literature but, even better, find a friendly expert and get instruction “from the horse’s mouth”—it gives more insight more quickly. As well as looking forward, and being alert to new developments, you should not forget the past. Many powerful mathematical results from earlier eras have 4 Princeton Companion to Mathematics Proof got buried and have been forgotten, coming to light only when they have been independently rediscovered. These results are not easy to find, partly because terminology and style change, but they can be gold mines. As usual with gold mines, you have to be lucky to strike one, and the rewards go to the pioneers. Independence At the start of your research your relationship with your supervisor can be crucial, so choose carefully, bearing in mind subject matter, personality, and track record. Few supervisors score highly on all three. Moreover, if things do not work out well during the first year or so, or if your interests diverge significantly, then do not hesitate to change supervisors or even universities. Your supervisor will not be offended and may even be relieved! Sometimes you may be part of a large group and may interact with other members of the faculty, so that you effectively have more than one supervisor. This can be helpful in that it provides different inputs and alternative modes of work. You may also learn much from fellow students in such large groups, which is why choosing a department with a large graduate school is a good idea. Once you have successfully earned your PhD you enter a new stage. Although you may still carry on collaborating with your supervisor and remain part of the same research group, it is healthy for your future development to move elsewhere for a year or more. This opens you up to new influences and opportunities. This is the time when you have the chance to carve out a niche for yourself in the mathematical world. In general, it is not a good idea to continue too closely in the line of your PhD thesis for too long. You have to show your independence by branching out. It need not be a radical change of direction but there should be some clear novelty and not simply a routine continuation of your thesis. Style In writing up your thesis your supervisor will normally assist you in the manner of presentation and organization. But acquiring a personal style is an important part of your mathematical development. Although the needs may vary, depending on the kind of mathematics, many aspects are common to all subjects. Here are a number of hints on how to write a good paper. (1) Think through the whole logical structure of the paper before you start to write. (2) Break up long complex proofs into short intermediate steps (lemmas, propositions, etc.) that will help the reader. (3) Write clear coherent English (or the language of your choice). Remember that mathematics is also a form of literature. (4) Be as succinct as it is possible to be while remaining clear and easy to understand. This is a difficult balance to achieve. (5) Identify papers that you have enjoyed reading and imitate their style. (6) When you have finished writing the bulk of your paper go back and write an introduction that explains clearly the structure and main results as well as the general context. Avoid unnecessary jargon and aim at a general mathematical reader, not just a narrow expert. (7) Try out your first draft on a colleague and take heed of any suggestions or criticisms. If even your close friend or collaborator has difficulty understanding it, then you have failed and need to try harder. (8) If you are not in a desperate hurry to publish, put your paper aside for a few weeks and work on something else. Then return to your paper and read it with a fresh mind. It will read differently and you may see how to improve it. (9) Do not hesitate to rewrite the paper, perhaps from a totally new angle, if you become convinced that this will make it clearer and easier to read. Wellwritten papers become “classics” and are widely read by future mathematicians. Badly written papers are ignored or, if they are sufficiently important, they get rewritten by others.
We are very happy to have Prof. Klaus Müller-Dethlefs to give us a great report on Non-covalent interactions studied by mass-resolved ZEKE spectroscopy: the future . He is a gentleman with a very positive attitude towards the life and has great sense of humor . The information he brought to us is more than we could imagine. However, I am going to share three important points which seems to be a sunshine that shines down to me: First of all,it will be much better if we contact with other academic students who belong to another filed, communication always seems to be a good way to get more inspiration. Secondly,learn to enjoy the beautiful life will do good to your research. Last but not the least,your advisor would open a door and say get out of here, and the world is open for you, no excuses, you must save the world! http://kyybgxx.cic.tsinghua.edu.cn/kybg/xsgg/detail.jsp?boardid=35seq=12986 报告题目: Non-covalent interactions studied by mass-resolved ZEKE spectroscopy: the future 报告人: Prof. Klaus Müller-Dethlefs Founding Director of The Photon Science Institute and School of Chemistry The University of Manchester，United Kingdom 报告时间: 2013-08-30 10:30 报告地点: 理科楼三楼报告厅 主办单位: 物理系 简介: we are reviewing the ZEKE method and its mass-selective variant, Mass Analysed Threshold Ionisation, MATI, in order to measure dissociation energies of molecular clusters with spectroscopic precision. In the near future, our studies will be extended to the systematic measurement of non-covalent stacking interactions in polycyclic aromatic dimers up to the coronene-dimer, a nano-graphene analog. This will be accompanied by high-level computations using coupled-cluster expansion theory up to CCSDT(Q). The goal is to establish benchmarks for the reliable application of ab initio calculations to very rage non-covalently bound supramolecular systems.
Posted by honuhawaii (221) 22 Nov 2011 to esi83: Hi - A couple of thoughts. I am in a field where conferences outweigh publications as well, and do not have too much to say in terms of peer-reviewed publications for myself. Also, Zhang Associates is my attorney. My NIW case was submitted in January, and I just received and forwarded to my attorney the response to my RFE. Therefore, I am familiar with all your issues, and this is what I will say. Please do watch my case - I expect to receive a decision in the next month or so, and I do hope it is a good one - that will tell you whether to believe my recommendations or not, since I myself have no faith in these till I learn for sure that they worked for me! :) 1. Without peer reviewed publications, you have to move mountains to justify to an immigration officer that you are NIW worthy. While I had very impressive letters, what the RFE boiled my case down to was insufficient publications/citations, and therefore, insufficient evidence of impact on the field. 2. The solution to my problem was thinking outside the box to demonstrate national influence without citations. I contacted people around the country who have talked to me, implemented my strategies, and benefited from my work to demonstrate impact. So you may want to start thinking about who attended your talks/posters, and who took your ideas and did something with them in their own areas, and get letters from those people. 3. Zhang Associates is timely, and very efficient. They were good about providing examples, and even editing the drafts I wrote. The problem with them was with thinking outside the box. I found that I had to do that thinking for myself. They didn't have a lot of experience with cases where people had demonstrated national influence without citations. Having said that, my attorney did share one example of an engineer who responded to an RFE about lack of national influence by submitting 100s of emails from people who had asked his advice on various matters over the years, and were grateful for what they had learned, and described how they implemented his suggestions into their work. So get your out of the box thinking hat on - you need to demonstrate that your work has influenced that of other people. Outside of citations, how would you best go about the process of demonstrating that? Remember, the proof is probably in the pudding, but the burden of showcasing it is entirely yours to bear. Retaining Zhang Associates will not change that burden much. Finally, while it is a good idea to send them your letter drafts before sending them off to people for their signatures, do review them - sometimes the statements they add in may not be appropriate, or may repeat themselves from one letter to another. In summary, good attorneys, but you need to be the champion of your own cause, and be an out of the box type of thinker. Good luck! Posted by gctracker250 (45) 23 Nov 2011 I think you are ok for NIW, though close to borderline. You can make a stronger NIW case if you can get your publication count and citation count higher. But letters will matter a lot too ... get good, independent, and international letters. When submitting a letter, include the CV of the writer to show that he or she is an expert in the field. ( reply ) Posted by jingyanwang (2) 2 hours 23 minutes ago Hi all, I'm working as a postdoc in US with a J1 visa, and I obtained my PhD on computer science from China. Currently, I have: -Publications: 22 first author papers, including 12 journal papers (8 indexed by SCI), 9 conference papers, and 1 book chapter, -Citations: 23 non-self citations to my first author papers, -Review: 12 invited review to papers of others (9 of them are SCI indexed journal paper), Do you think I have a chance for NIW green card? Thanks a lot! ( reply ) ( report this ) Posted by hickory (469) 2 hours 11 minutes ago to jingyanwang: Obtain some real strong letters that outline how important your studies are for the US. You have just about 2 citations per peer reviewed publication and that can be an issue when you try to prove that your studies are well recognized by your peers. In such a situation, exhibiting your works' national importance is the way to go. I also see that you can comfortably claim publications, and reviewing others' work. But carefully consider the requirement stated in this page for NIW - http://tinyurl.com/yzrp539 Hope you can ensure that you can fulfill 3 of the requisites. All the best. ( reply ) ( report this ) Posted by jingyanwang (2) 3 minutes ago to hickory: Thank you very much for your kindly reply. You are right --- my main weakness is the citation. Maybe I should apply later when I enough citations, since some of my papers are published very recently. But how many citations could make my case safe? 40, or 60 citations? Or more? Best regards! ( reply ) ( edit ) ( delete ) ( report this ) Posted by hickory (472) 18 minutes ago to jingyanwang: There is in fact no rule of thumb for citation numbers with respect to NIW. I only had about 60 when I applied for NIW in 2010. If you go through the profiles of various NIW applicants on trackitt, there are quite a few who have about 20-30 citations. However, as I wrote earlier, the burden of proving that your work benefits and will benefit the nation is upon you. And the expert support letters and your own cover letter can do that job quite well. Regards and wishes. ( reply ) ( report this )
Fornew readers and those who request to be “ 好友 good friends” please read my 公告 栏 first. Another 12 months havepassed since my last update. The list is now up-to-date as of Nov 10, 2017 For readers seeking help or advice (4) http://blog.sciencenet.cn/blog-1565-570182.html For Readersseeking help and advice (III) http://blog.sciencenet.cn/blog-1565-454292.html , For Readers seeking help and advice (II) http://blog.sciencenet.cn/home.php?mod=spaceuid=1565do=blogid=376393 and ForReaders seeking help and advice http://www.sciencenet.cn/m/user_content.aspx?id=274536 Look over the lastarticle above and the list of topics contained therein. You often will findanswers there.
Xiao Yxxx, If you want to publish a paper based on modeling results, the first thing to show is OBSERVATION. If the authors do not show tidal observations in the Taiwan Strait, how can readers tell if the model is doing anything correctly? Think about this. Zuojun
Fornew readers and those who request to be “ 好友 good friends” please read my 公告 栏 first. Another 12 months have passed since my last update.The list is now up-to-date as of March 11, 2013. (Note added 3/21/2016: The list is now up-to-date as of Nov. 10, 2017 For Readers seeking help and advice (III) http://blog.sciencenet.cn/blog-1565-454292.html , For Readers seeking help and advice (II) http://blog.sciencenet.cn/home.php?mod=spaceuid=1565do=blogid=376393 and For Readers seeking help and advice http://www.sciencenet.cn/m/user_content.aspx?id=274536 Look over the last article above and the list of topics contained therein. You often will find answers there.
I am an ocean modeler by training. I know what my model can and cannot do. I try my best to validate my model output using observations, so should you.
目录 1 How to Read a Paper 2 How to read a research paper 3 4 Whitesides Group: Writing a Paper 5 美国教授对中国学生写英文文章的建议 6 Prof. S. Keshav: http://blizzard.cs.uwaterloo.ca/keshav/wiki/index.php/Main_Page How to Read a Paper S. Keshav ABSTRACT Researchers spend a great deal of time reading research papers. However, this skill is rarely taught, leading to much wasted effort. This article outlines a practical and efficient three pass method for reading research papers. I also describe how to use this method to do a literature survey. Keywords: Paper, Reading, Hints. 1. INTRODUCTION the reanson for reading papers: 1) to review them for a conference or a class, 2) to keep current in their field, or for a literature survey of a new field. 2. THE THREE-PASS APPROACH The key idea : should read the paper in up to three passes, instead of starting at the beginning and plowing your way to the end. Each pass accomplishes specific goals and builds upon the previous pass: 1) The first pass gives you a general idea about the paper. 2) The second pass lets you grasp the paper's content , but not its details. 3) The third pass helps you understand the paper in depth . 2.1 The first pass The first pass is a quick scan to get a bird's-eye view of the paper. You can also decide whether you need to do any more passes. This pass should take about five to ten minutes and consists of the following st eps: 1. Carefully read the title, abstract, and introduction 2. Read the section and sub-section headings, but ignore everything else 3. Read the conclusions 4. Glance over the references, mentally ticking off the ones you've already read At the end of the rst pass, you should be able to answer the five Cs : 1. Category: What type of paper is this? A measurement paper? An analysis of an existing system? A description of a research prototype? 2. Context: Which other papers is it related to? Which theoretical bases were used to analyze the problem? 3. Correctness: Do the assumptions appear to be valid? 4. Contributions: What are the paper's main contributions? 5. Clarity: Is the paper well written? Using this information, you may choose not to read further. 2.2 The second pass In the second pass, read the paper with greater care, but ignore details such as proofs. It helps to jot down the key points, or to make comments in the margins, as you read. 1. Look carefully at the figures, diagrams and other illustrations in the paper. Pay special attention to graphs. Are the axes properly labeled? Are results shown with error bars, so that conclusions are statistically significant? Common mistakes like these will separate rushed, shoddy work from the truly excellent. 2. Remember to mark relevant unread references for further reading (this is a good way to learn more about the background of the paper). The second pass should take up to an hour. After this pass, you should be able to grasp the content of the paper. You can now choose to: (a) set the paper aside, hoping you don't need to understand the material to be successful in your career, (b) return to the paper later, perhaps after reading background material (c) persevere and go on to the third pass. 2.3 The third pass The key to the third pass is to attempt to virtually re-implement the paper: that is, making the same assumptions as the authors, re-create the work. By comparing this re-creation with the actual paper, you can easily identify not only a paper's innovations, but also its hidden failings and assumptions. This pass can take about four or ve hours for beginners, and about an hour for an experienced reader. 3. DOING A LITERATURE SURVEY What papers should you read papers in unfamiliar fields? Here is how you can use the three-pass approach to help. 4. EXPERIENCE 5. RELATED WORK 个人点评： 精彩的建议，文章值得反复阅读 paper-reading.pdf How to read a research paper the goal for reading paper: to understand the scientific contributions the authors are making. Notice: This is not an easy task. It may require going over the paper several times. Expect to spend several hours to read a paper some initial guidelines for how to read a paper: Read critically: asking appropriate questions: 1) If the authors attempt to solve a problem, are they solving the right problem? 2) Are there simple solutions the authors do not seem to have considered? 3) What are the limitations of the solution (including limitations the authors might not have noticed or clearly admitted)? 4) Are the assumptions the authors make reasonable? 5) Is the logic of the paper clear and justifiable, given the assumptions, or is there a flaw in the reasoning? 6) If the authors present data, did they gather the right data to substantiate their argument, and did they appear to gather it in the correct manner? 7) Did they interpret the data in a reasonable manner? Would other data be more compelling? Read creatively: Reading a paper critically is easy, in that it is always easier to tear something down than to build it up. Reading creatively involves harder, more positive thinking. 1) What are the good ideas in this paper? 2) Do these ideas have other applications or extensions that the authors might not have thought of? 3) Can they be generalized further? 4) Are there possible improvements that might make important practical differences? 5) If you were going to start doing research from this paper, what would be the next thing you would do? Make notes as you read the paper: Mark the data help the first time you read a paper and pay big dividends when you have to re-read a paper after several months. After the first read-through, try to summarize the paper in one or two sentences. Almost all good research papers try to provide an answer a specific question. 1) If you can succinctly describe a paper, you have probably recognized the question the authors started with with and the answer they provide 2) Once you have focused on the main idea, you can go back and try to outline the paper to gain insight into more specific details. 3) then deepen your outline by summarizing the three or four most important subpoints of the main idea. If possible, compare the paper to other works. Are the ideas really novel, or have they appeared before? It is worth mentioning that scientific contributions can take on many forms. Some papers offer new ideas; others implement ideas, and show how they work; others bring previous ideas together and unite them under a novel framework. Knowing other work in the area can help you to determine which sort of contribution a paper is actually making. to provide a short, one page review of a paper. Keeping the above in mind as you read the paper should make the process easier. Your one page review should include the following: a one or two sentence summary of the paper. a deeper, more extensive outline of the main points of the paper, including for example assumptions made, arguments presented, data analyzed, and conclusions drawn. any limitations or extensions you see for the ideas in the paper. your opinion of the paper; primarily, the quality of the ideas and its potential impact. 个人点评： 好阅读hints! ReadPaper.pdf Whitesides Group: Writing a Paper George M. Whitesides Dept of Chemistry and Chemical Biology, Harvard University 1 . What is scientific paper? A paper is an organized description of hypotheses, data and conclusions, intended to instruct the reader. Papers are a central part of research. Realize that your objective in research is to formulate and test hypotheses, to draw conclusions from these tests, and to teach these conclusions to others. Your objective is not to “collect data.” A paper is not just an archival device for storing a completed research program, it is also a structure for planning your research in progress . If you clearly understand the purpose and form of a paper, it can be immensely useful to you in organizing and conducting your research. A good outline for the paper is also a good plan for the research program. You should write and rewrite these plans/outlines throughout the course of the research. At the beginning, you will have mostly plan; at the end, mostly outline. The continuous effort to understand, analyze, summarize, and reformulate hypotheses on paper will be immensely more efficient for you than a process in which you collect data and only start to organize them when their collection is“complete.” 2.Outlines 2.1 The reason for outlines. I emphasize the central place of an outline in writing papers, preparing seminars, and planning research. I especially believe that for you, and for me, it is most efficient to write papers from outlines. An outline is a written plan of the organization of a paper, including the data on which it rests. You should, in fact, think of an outline as a carefully organized and presented set of data, with attendant objectives, hypotheses and conclusions, rather than an outline of text. An outline itself contains little text. If you and I can agree on the details of the outline (that is, on the data and organization), the supporting text can be assembled fairly easily. If we do not agree on the outline, any text is useless. Much of the time in writing a paper goes into the text; most of the thought goes into the organization of the data and into the analysis. It can be relatively efficient to go through several (even many) cycles of an outline before beginning to write text; writing many versions of the full text of a paper is slow. All the writing that I do – papers, reports, proposals (and, of course, slides for seminars)- I do from outlines. I urge you to learn how to use them as well. 2.2 How should you construct an outline? The classical approach is to start with a blank piece of paper, and write down, in any order, all important ideas that occur to you concerning the paper. Ask yourself the obvious questions:“ Why did I do this work?” “What does it mean?”“What hypothesis did I mean to test?”“What ones did I actually test?”“What were the results?”“Did the work yield a new method or compound? What?”“What measurements did I make?”“What compounds? How were they characterized?” Sketch possible equations, figures, and schemes. It is essential to try to get the major ideas written down. If you start the research to test one hypothesis, and decide, when you see what you have, that the data really seem to test some other hypothesis better, don’t worry. Write them both down, and pick the best combinations of hypotheses, objectives and data. Often the objectives of a paper when it is finished are different from those used to justify starting the work. Much of good science is opportunistic and revisionist. When you have written down what you can, start with another piece of paper and try to organize the jumble of the first one. Sort all of your ideas into three major heaps (A-C). A) Introduction Why did I do the work? What were the central motivations and hypotheses? B) Results and Discussion What were the results? How were compounds made and characterized? What was measured? C) Conclusions What does it all mean? What hypotheses were proved or disproved? What did I learn? Why does it make a difference? Next, take each of these sections, and organize it on yet finer scale. Concentrate on organizing the data. Construct figures, tables, and schemes to present the data as clearly and compactly as possible. This process can be slow – I may sketch a figure 5-10 times in different ways, trying to decide how it is most clear (and looks best aesthetically). Finally, put everything—outline of sections, tables, sketches of figures, equations – in good order. When you are satisfied that you have included all the data (or that you know what additional data you intend to collect), and have a plausible organization, give the outline to me. Simply indicate where missing data will go, how you think (hypothesize) they will look, and how you will interpret them if your hypothesis is correct. I will take this outline, add my opinions, suggest changes, and return it to you. It usually takes 4-5 repeated attempts (often with additional experiments) to agree on an outline. When we have agreed, the data are usually in (or close to) final form (that is, the tables, figures, etc., in the outline will be the tables, figures,…in the paper.) You can then start writing, with some assurance that much of your prose will be used. The key to efficient use of your and my time is that we start exchanging outlines and proposals as early in a project as possible. Do not, under any circumstances, wait until the collection of data is “complete” before starting to write an outline. No project is ever complete, and it saves enormous effort and much time to propose a plausible paper and outline as soon as you see the basic structure of a project. Even if we decide to do significant additional work before seriously organizing a paper, the effort of writing an outline will have helped to guide the research. 2.3 The outline What should an outline contain? 1.Title: 2.Authors: 3. Abstract: Do not write an abstract. That can be done when the paper is complete. 4.Introduction: The first paragraph or two should be written out completely. Pay particular attention to the opening sentence. Ideally, it should state concisely the objective of the work, and indicate why this objective is important. In general, the Introduction should have these elements: * The objectives of the work. * The justification for these objectives: Why is the work important? * Background: Who else has done what? How? What have we done previously? * Guidance to the reader. What should the reader watch for in the paper? What are the interesting high points? What strategy did we use? * Summary conclusion. What should the reader expect as conclusion? In advanced versions of the outline, you should also include all the sections that will go in the Experimental section (at this point, just as paragraph subheadings). 5.Results and Discussion. The results and discussion are usually combined. This section should be organized according to major topics. The separate parts should have subheadings in boldface to make this organization clear, and to help the reader scan through the final text to find the parts that interest him or her. The following list includes examples of the phrases that might plausibly serve as section headings: * Synthesis of Alkane Thiols * Characterization of Monolayers * Absolute Configuration of the Vicinal Diol Unit * Hysteresis Correlates with Roughness of the Surface * Dependence of the Rate Constant on Temperature * The Rate of Self-Exchange Decreases with the Polarity of the Solvent Try to make these section headings as specific and information-rich as possible. For example, the phrase “The Rate of Self-Exchange Decreases with The Polarity of The Solvent” is obviously longer than “Measurement of Rates,” but much more useful to the reader. In general, try to cover the major common points: * Synthesis of starting materials * Characterization of products * Methods of characterization * Methods of measurement * Results (rate constants, contact angles, whatever) In the outline, do not write any significant amount of text, but get all the data in their proper place: any text should simply indicate what will go in that section. * Section Headings * Figures (with captions) * Schemes (with captions and footnotes) * Equations * Tables (correctly formatted) Remember to think of a paper as a collection of experimental results, summarized as clearly and economically as possible in figures, tables, equations, and schemes. The text in the paper serves just to explain the data, and is secondary. The more information that can be compressed into tables, equations, etc., the shorter and more readable the paper will be. 6.Conclusion. In the outline, summarize the conclusions of the paper as a list of short phrases or sentences. Do not repeat what is in the Results section, unless special emphasis is needed. The Conclusions section should be just that, and not a summary. It should add a new, higher level of analysis, and should indicate explicitly the significance of the work. 7. Experimental. Include, in the correct order to correspond to the order in the Results section, all of the paragraph subheadings of the Experimental section. 2.4 In summary: * Start writing possible outlines for papers early in a project. Do not wait until the “end”. The end may never come. * Organize the outline and the paper around easily assimilated data – tables, equations, figures, schemes – rather than around text. * Organize in order of importance, not in chronological order. An important detail in writing paper concerns the weight to be given to topics. Neophytes often organize a paper in terms of chronology: that is, they recount their experimental program, starting with their cherished initial failures and leading up to a climactic successful finale. This approach is completely wrong. Start with the most important results, and put the secondary results later, if at all. The reader usually does not care how you arrived at your big results, only what they are. Shorter papers are easier to read than longer ones. 3. Some Points of English Style 2004 am whitesides' group writing a paper.pdf 中文版（译者有省略）： 科学论文的写作.pdf 个人点评： 一篇值得反复阅读的好文章 美国教授对中国学生写英文文章的建议 个人点评： 没有看，写完文章后再仔细比较 美国教授对中国学生写英文文章的建议.pdf the order to read a scientific paper: abstract - discussion - background - result http://www.lib.purdue.edu/content/tutorials-scientific-paper how-to-read-a-paper.pdf
A Piece of Advice for Mr. Huang Xiuqing by Yang Wenxiang Forget these unhappy things. You need not to be so sorry. If someone feels that he/she is wasting his/her time to read your articles, you may let him/her know this thing, it is he/she to select and read these articles, not you make them to. Reference: 1. 黄秀清 . 在科学网写博客，也会 “ 谋财害命 ” ？ http://bbs.sciencenet.cn/home.php?mod=spaceuid=480705do=blogid=414985
SOME MODEST ADVICE FOR GRADUATE STUDENTS 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 advisors might become unsupportive - or even hostile. Plan for alternatives. Nobody Cares About You In fact, some professor 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 hogwash until the author managed 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 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 on your own research. You will continually be asking yourself, What and 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 Ph.D. 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 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 Barriers 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 know 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 Ph.D. and it's 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 your probably are good enough after all. 1 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. 2 Graduate school is only one of the tools that you have at hand for shaping your 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 Ph.D. 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 be 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 counter-intuitive, 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 the 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. 5 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 fails for practical reasons. 6 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 or terror at this point. Don't worry - it goes on like this for awhile, then it gradually gets worse. 7 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. 8 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 interest. 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. 2A critique of the foundations of an important body of research. Again, rare and valuable and a sure winner if properly executed. 3The 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 there are graduate students. The four types listed serve as limited cases of the good, the bad and the ugly. Doctoral work is a chance for you to try you had at a number of different research styles and to discover which suits 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 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, referred 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 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 project 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 the 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 and Publish 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 a 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 Ph.D. 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 Ph.D. 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. Postscript This comment was originally entitled Cynical aids towards getting a graduate degree, or psychological and practical tools to use in acquiring and maintaining control over your own life. It originated as a handout for the Ecolunch Seminar in the Department of Zoology, University of California, Berkeley, on a Monday in the spring of 1976. Ecolunch was, and is, a Berkeley institution, a forum where graduate students present their work in progress and receive constructive criticism. At the start of the semester, however, no one is ready to talk. This was such a time. On Friday morning at Museum Coffee, Frank Pitelka, who was in charge of Ecolunch for that semester, asked me to make the presentation on the following Monday. Asked is probably a misleading representation of Frank's style that morning. Frank bullied me into it. I had just given a departmental seminar on the Ph.D. work I had done at British Columbia, and did not have much new to say about biology. Frank's style brought out the rebel in me. I agreed on the condition that I had complete freedom to say whatever I wanted to, and that the theme would be advice to graduate students. Frank agreed without apparent qualms. Then I charged upstairs to Ray Huey's office to plot the attack. I whipped out an outline, Ray responded with a more optimistic and complementary version (see the following Commentary article), and I wrote a draft at white heat that afternoon. We felt like plotters. We were plotters. There were acts of self-definition in the air. On Monday, I recall that I made a pretty aggressive presentation in which, to emphasize how busy faculty members were, I kept looking at my watch. Near the end I glanced at my watch one last time, said I had to rush off to an appointment, left the room suddenly without taking questions, and slammed the door. They waited. I never came back, but Ray took over and presented his alternative view. Ray told me later that Bill Lidicker turned to him and said, You mean he's not coming back? I wasn't. Fortunately, they took it well. They were and are a group of real gentlemen. I mention these things to explain the tone of our pieces. We would not write them that way now, having been professors ourselves for some years. We never intended to publish them, having regarded the presentations as a one-time skit, but our notes were xeroxed and passed around, and eventually they spread around the United States. In the fall of 1986 I got a letter from Pete Morin at Rutgers suggesting that we publish the notes. Its survival for ten years in the graduate student grapevine convinced me that there might actually be a demand for them. I had lost my original, and Pete kindly sent me a copy, which turned to be a nth generation version with marginal notes by a number of different graduate students. On rereading it, I find that I agree with the basic message as much as ever, but that many of the details do not apply outside the context of large American universities. Ten years later, I have one after-thought. 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, then 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 enough time to do the job right. Acknowledgments Thanks to Frank Pitelka for providing an opportunity, to Ray Huey for being a coconspirator 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 during the last decade, and to Pete Morin for suggesting that we write them for publication. Some Useful References Day, R.A. 1983. How to write and publish a scientific paper. Second edition. ISI Press, Philadelphia, Pennsylvania, 181 pp. wise and witty. Smith, R.V. 1984. Graduate research - a guide for students in the sciences. ISI Press, Philadelphia, Pennsylvania, USA. 182 pp. complete and practical. Strunk, W., Jr., and E.B. White. 1979. The elements of style. Third Edition. Macmillan, New York, New York, USA. 92 pp. the paradigm of concision. Stephen C. Stearns Department of Ecology and Evolutionary Biology Yale University P.O. Box 208106 New Haven, CT 06520-8106 USA
Giving Advice: Enough Is Enough After Three Solar Cycles by M. Mendillo appeared on EOS (1 Sep 2009). A comment by David Stern and a reply followed on 26 Jan 2010. I thought all scientists should read these articles, young or old, in China or in the U.S. Here they are: Giving Advice (1) Giving Advice (2) and (3)
标签: advice
