首先，我不是Ph.D，但也在做一些研究工作。觉得这篇文章讲的很不错，就贴出来，间或有点自己的理解。
How to do research? And Related Issues of Ph.D Education
"Can you tell me how to do research?",
"Please tell me what topics should I pick to do my ph.d.thesis? "
are two questions I periodically receive from young researchers and students in China.
呼呼，是中国学生的两大困惑~~
There are two difficulties associated with answering these two questions.
1. The first question is open-ended. To answer it honestly and accurately will
require several hours of explanation. In fact, the process could take several
years of face-to-face interaction between an advisor and a ph.d student. This is
really what a ph.d. education involves. It is not the number of courses taken or
the number of papers published. But something about the quality of and taste
in research. I'll have more to say about this point below in connection with
trying to answer this first question here .
第一个问题难倒我了，太复杂。先说明的是，Ph.D教育是一个长期的学生与导师面对面交流的过程。相对你修了多少课，发了多少paper而言，研究的质量更加重要。这表明，你只挂个牛逼导师的名字是不够的，还要互相交流学习；在会议和期刊上水N多文章是没有多大意思的，更重要的是研究的质量。在今天大家都在争着发paper的形势下，这点是应该注意的。
2. Behind the second question lie a unintentional misconception by many young
workers about "research" that probably has its origin in the martial arts novels
of Chinese literature (武侠小说). In typical novels of this genre, the
hero/heroine learns powerful martial arts technique through some secret
magical instruction passed down from a master or a long lost instruction book.
As a result, overnight s/he was able to defeat his/her enemy and achieve
success. Thus, many students are constantly looking for that "magical
formula" for research. Another common criticism of Chinese university
education by Westerners is that most students learn to answer questions or
pass exams extremely well, but there is little training in posing questions and
formulating problems which are really the important parts and more than half
of research. Growing up in such environment, it is natural for Chinese
students to seek the magical formula for research success. It is also my
purpose to address this issue here.
看来作者对武侠小说也很有研究，不过作者说了，武功秘籍是没有的，认为中国的大学生在回答问题和考试方面做的非常棒，但是缺乏提出问题，将问题形式化以发现问题的主要和实质内容的训练，而这是研究的一大半内容。由于我们所处的教育环境，也就可以理解我们为何如此渴望秘籍了。其实我们还真是有这个毛病，总想着灵光一闪就有了思路，马上动手，然后发paper，只是这灵光却没闪过，因为我们没有能发现问题，发现问题的本质。眼毒阿。
To give an answer to the first question, you can approach it at three levels. At the first
level, your aim is to be that one scientific person in a century, e.g., the discoverer of the
theory of relativity. I have no experience or advice to give at that level. All I can say is
"good luck". At the next level, you want to be the founder of a research topic or make the
breakthrough on a difficult problem. Again, there is no magic here. For otherwise,
breakthrough will become commonplace. However, I do have one suggestion that worked
well for me and which is generally applicable. This I offer below:
针对个人的追求层次不同，回答第一个问题。一、树立成立世纪科学家的目标，如相对论发现者。这个是讲“运气”的，就是看人品啦。二、开创一个研究课题或者解决超级难题，比如哥德巴赫猜想啦，这个也很不容易，否则重大突破就太轻松了，科技进步一等奖可不是弄着玩的。但是作者根据自己的经历，还是可以提供一些通用的建议的。
I participated in a panel discussion 8 years ago which involves my answers to several
general questions posed to me at the panel and which still apply today. ( The 1999 IEEE
Conference on Decision and Control panel on "At the Gate of the Millennium – Are we
in control?" Published in IEEE Control Systems Magazine Vol.20, #1, Feb, 2000)
作者参加过一个千年之门小组讨论会，提出过这方面的问题。这个讨论会应该是大师级参加的吧。要不找来瞧瞧？？下面也有滴。。。 下面开始引述：
BEGINNING OF QUOTE
1. What are the 5 most notable research results in systems and control theory in the
past 100 years?
The "test of time" and traditions of history rule out mentioning anything
developed in the past 25 years or involving living persons. Furthermore, scientific
discovery often is a matter of standing on the shoulder of others. To single out specific
results do not seem to be fair to others who laid the foundation. Instead, I propose to list
couple of ideas that seems to me have influenced the development of our field in a major
way
1. The fundamental role of probability and stochastic process in system work.
2. The concept of what constitutes a solution to a problem, namely, that which can
be reduced to another routinely solved problem such as numerical integration
3. The notion of dynamics and feedback in all their ramifications
The first item represents how knowledge from outside the field influenced our research
while the third states what specific concepts our field contributed to other fields. The
second item deals with how practices in science and mathematics are changed by
technology. These notions are generic and have parallel in other topics and fields.
在过去的百年里系统控制理论方面有哪5个最瞩目的研究成就？？科学发现通常是要站在巨人肩膀上的，只关注结果对于领域的奠基人来说是不公平的，可惜的是我们总是关注台上手捧鲜花的人，他们身后的前辈、同事总是被我们轻易的遗忘。
2. What are future research milestones (for the next 5-10 years) which will have a
most significant impact on the field? Comment on what we should be doing now
and in the near future to make such accomplishments possible. Also discuss your
thoughts on:
i.Education issues. How should we be training our students to meet the future
challenges?
ii.Technology issues. What we see coming up that will change the control
landscape.
iii.Computational tools.
下面5--10年的研究里程碑会是什么？？完成这些研究我们现在和以后要做什么？？
Scientific crystal balling has a notorious record in the past. The dust heap of past
predictions is filled with gross miscalculations and estimations by noted scientists with
the best of intentions. Let me try to approach the question "what's next in control systems
in the 21st century?" in a somewhat different way. During my travel and lectures, I am
often asked by young scientist/engineers starting out in their careers on what are
profitable avenues of research to pursue. One is often tempted to point to ones own
current research topic, which by definition must be the most interesting things to do.
However, this is selfish and dangerous advice. My considered advice, which I myself
have followed, is this:
"GO FIND A REAL WORLD PROBLEM THAT A GROUP OF PEOPLE IS
EAGER TO SOLVE, THAT HAPPENS TO INTEREST YOU FOR WHATEVER
REASON, AND THAT YOU DON'T KNOW MUCH ABOUT.
MAKE A COMMITMENT TO SOLVE IT BUT NOT A COMMITMENT
TO USE TOOLS WITH WHICH YOU HAPPEN TO BE FAMILIAR"
什么是这样的方向呢？？总有人说是自己当前研究的课题，这是相当自负和危险的意见。我认为应该是：发现一个大家亟待解决的现实问题，你对这个问题感兴趣，而知之不多，努力去解决它但不要用熟悉的工具。
Such an approach has several immediate advantages. First, if you are successful
then you have some free built-in Public Relations. Unsolicited testimonial by others is the
best kind of publicity for your work. Second, most probably you have discovered
something new or have found a new application of existing knowledge. In either case,
you can try to generalize such discovery later into a fruitful research area for which you
will be credited with its founding. Third, in a new problem area there is generally less
legacy literature you will have to learn and reference. Fourth, a new problem area is like a
newly discovered mine. For the same effort you can pick up more nuggets lying near the
surface than digging deep in a well-worked out mineshaft. By the same reasoning, the
probability of serendipity at work is also by definition higher in a new area. Lastly, even
if you are unsuccessful in solving the original problem, you will have at the very
minimum learned something new which will increase the chance of your success in
future tries.
这种方法有很多直接的好处。首先，如果成功了你在公共关系上就有了基石，其次，你很可能发现了一些新的知识或者现有知识的新应用，不管怎么样你都会在接下来的工作中扩大这种发现，使他成为你的研究成果并获得认可，第三，新的领域中通常每那么多的优秀著作可供学习参考；第四，新领域如同新发现的矿藏，可以挖出很多宝贝的；最后，即使你没有成功，至少你也学了一些新的知识，对以后的成功总有裨益。
My own personal experiences whether it was differential games, manufacturing
automation, perturbation analysis in discrete event simulation, or ordinal optimization
reinforces the above belief. Above all, faith in the ability of the future generation of
scientists and engineers makes me an optimist in saying, "the best is yet to be, you haven't
seen nothing yet". It is fine to make predictions and to look forward, but there is no need
to get too obsessed with divining the future.
要相信以后会成为科学家、工程师，这样就可以乐观的说“还不是最好的，你现在什么都不是呢”，可以向前看做一些预测，但不要看太远，不然就是好高骛远了。
As far as technology and computational issues are concerned, I believe I have
already given my answer in the recent op-ed piece published in the June '99 issue of the
IEEE Control System Magazine "The No Free Lunch Theorem and the Human-Machine
Interface". I shall simply add by repeating what I said at my Bellamn Award acceptance
"the subject of control which is based on mathematics, enabled by computers, is about to
have a new birth of freedom under computational intelligence".
END OF QUOTE.
I now wish to elaborate on the last sentence in the above advice about making a
commitment. In trying to solve a problem, one is always tempted to use tools with which
one is familiar. This is very natural. Our training in school for the most part deals with
tools. Exercises associated with such learning are always designed to fit these tools. As a
result when we tackle a problem outside the textbook, our first instinct is to reach for
these tools.
But as engineers who ultimately must solve real world problems or as academic
engineers who aspire to pioneer breakthrough research, such an approach is often not the
best way. Basically, you are "a solution in search of a problem to fit". Too often, we bend
the problem to fit the solution.
尝试解决问题时，我们总是试着用我们熟悉的工具，这是很自然的，我们接受的训练很大部分也是去适应这些工具。但是当工程师解决现实世界的问题或者学术工程师渴求成为突破性研究的先驱时，这种方式往往不是最佳的。基本上，我们是在寻找解决问题的方案，更经常地，我们修正问题以适应我们的解决方案。这样其实我们偏离了原来的问题，不是用方法解决问题，而是让问题适应方法，偷懒了。
Instead, it has been my experience that we should take the problem as it presents itself
and not form any pre-conceived idea on how to solve it. Confronting a problem on its
terms promotes looking at it in the simplest terms since we have nothing but common
sense to guide us. New ideas and knowledge, the bloodline of research, are often
discovered this way. Such ideas in addition will be practically relevant and significant
since they are discovered in the process of solving a real world problem as opposed to
extending or generalizing a given mathematical formula.
事实上，我们应该按照问题的本来面目来对待它，不要形成任何先入为主的想法。原原本本地面对问题有助于以最简单的方式看待它，因为引领我们的只有常识。新的思想和知识通常就是这么发现的，这就是“研究的血统”(高贵的东东阿)。这些思想更加有实际意义，更加重要，因为它们诞生与实践之中，而不是扩展泛化给定的数学公式。嘿嘿实践论原理。
By the same token, when one derives a formula via analysis, it is useful to ask the
question: "how is this formula useful to an engineer/user? ". A user is not particularly
interested or impressed by the elegance of your derivation but more interested in how the
formula will help him; the relative importance of various parameters in the formula; any
critical threshold which affects performance, etc. A formula will only be used if the user
can understand its significance
In commerce, the adage is that to be successful, you must serve your customers well. As
an academic in an engineering department or a researcher in an industrial company, we
should always remember who are our ultimate customers and make a commitment to
serve them well.
同样的道理，如果你通过分析推导出一个公式，要先自问：“这个公式对使用者有用吗？”。使用者可不关心你的公式多么漂亮，他们更加关心对他们的工作有什么用，公式中各个参数的重要程度，影响性能的瓶颈等等。只有使用者明白了它的重要性，公式才是有用的。商业上，必须以“顾客是上帝”为宗旨才能成功，同样在学术上，也必须记得谁是我们最终的“顾客”，要把他们弄舒服了才行，不然就等着关门吧。
Finally, a purely theoretical paper no matter how elegant will be thoroughly understood
and appreciated by only a few people. But everyone can appreciate the significance of a
real world application. For academic engineers, if you want your work widely admired
and used, you must adapt your theory to practice and not the other way around.
最后，纯理论的论文不管可以多么容易彻底理解，被一小部分人欣赏。但所有人都喜欢现实应用的重要性。对于做学术的人，如果想要工作被广泛
Lastly, most of the published research by most of us belong to the third level which I
denote as incremental research within an established framework. These are still important
works. These efforts provide continuation and transfer of knowledge from one generation
to another, extension, addition and clarification our knowledge base, and above all
justification for our existence. To do this kind of research, you must learn the prior
literature by consulting reviews, tutorials, and related published papers. However, you
should be warned that even if you read the papers on the day they are published, you are
at least 18 month out of date due to the delays in reviewing and publishing. This is where
your advisor comes in and the reason to go to conferences. An advisor, expert in a given
area, is aware of the latest results in the area long before they are published. Other
researchers are eager to sent new and unpublished results to these experts/authorities for
comments and to establish priority. And to maintain his/her expertise, such advisor keeps
up with the literature. If you are students of such as advisor, you benefit accordingly.
Secondly, conference proceedings are faster form of publication than archival journals.
Also the real benefit of going to a conference is the chance to informally gather the latest
information on topics of research. When you are working on the cutting edge of a
research topic, you must spend effort to keep up communications with others interested in
the same topic. "closing the door in order to built a car" is not a recommended way to do
research which knows no national boundaries. The existence of the Internet ameliorated the
problem of information gathering and transmission for the individual to some extent.
Students in developing countries and developed countries are more on a even playing field.
However, there is nothing to replace the personal attention of an expert advisors and mentor.
我们发表的大多数文章属于第三层次的，是在已有框架下进行的增量研究。这些研究是重要的，可以传承知识，扩张、增加、廓清知识基础，检测现有的知识。要做这些工作，要阅读之前的著述，但是要注意的是，即使你读的是今天发表的文章，由于审阅发表的流程延时你也至少落后了18个月。在某个领域有经验的人都对最新的成果很敏感，在那些文章发表之前就进行跟踪，其它的研究人员也会把自己的成果发给他们征求意见，如果你的导师是这样的人，那就会获益良多；其次，会议要比期刊发表用的时间短。参加会议可以交流、获得最新的进展，紧跟潮流步伐，不然就陷入闭门造车的困境中了。互联网为大家提供了交流、分享信息的平台，但去参加会议仍然十分有必要。。。可惜我们的机会不多阿。。
Speaking about advisors and mentors, there are different philosophies on the role played
by a Ph.D thesis advisor. One extreme school of thought (rather prevalent in China but
rare in leading universities elsewhere) views the role of an advisor simply as a
grader/examiner. Students are supposed to be self-sufficient (自生自灭). The advisor
merely makes sure that all rules are observed, requirements satisfied and the student's
thesis meet certain minimal standards. This way, a person can supervise ten, twenty, or
even fifty Ph.D. students. This makes life easy for the advisor but is bad for the scientific
standards of the profession. It also tends to hide the incompetence of the advisor. At the
other extreme, the role of an advisor is more akin to that between a kung-fu master and
disciple – it is a very serious commitment and responsibility on the part of the advisor
lasting over many years and sometimes over a lifetime. In such cases, taking on a Ph.D.
student is a time consuming task for at least five years. The advisor works closely with
the student and tries to convey and teach many things that are not in the textbooks but
important to the student in his/her career and life development. An advisor working in
this Socrates' teaching mode can handle at most five or six Ph.D. students simultaneously
when he is working full time. My own philosophy is more inclined towards this old
fashioned school of thought since I believe except for geniuses, first rate scholars are
taught and created this way.
As to the standard used in a Ph.D. thesis, I have three:
a) Portion of the thesis must be accepted for publication in a leading journal (not
just any SCI listed journal) of the field. Top scholars of a field usually agree on
what set of journals are leading in a given field. This requirement is not only an
independent check of the contribution of the thesis but also serve to publicize the
product of the university to the world.
b) The advisor should learn something new from the student thesis.
c) The advisor should not be ashamed to admit in public that he supervised the thesis
since it is also a reflection of the standard and competence of the advisor.
导师和学生之间的互动关系。完全让学生自己弄是不行的，不负责的。。但是说实话，国内很多牛人都是挂个名，真正带学生的是手下的“小老板”，“大老板”都忙着行政、赚钱了，多少让人感觉愤懑，却又无能为力。所以我们很难有国际大师出现。
Admittedly, two of the three criteria are subjective and can lead to abuse. Only a healthy
system of peer review and established self-discipline by the profession can prevent abuse.
I also understand the current Chinese regulation for Ph.D. degrees requiring four
journal/conference publications. While this is excessive if strictly enforced (footnote: It
is more strict than any system in the world and certainly more than my own
requirements), I understand to some extent the rationale behind it. Until the quality of
Ph.D. advising becomes uniform through out the graduate schools, some form of
quantitative requirement will be necessary to prevent abuse and to insure a minimal
standard.
In short, there is no royal road to research success except focused hard work.
总而言之，言而总之，除了努力工作，要取得成功是没有捷径的。引用下华罗庚的话：“科学上没有平坦的大道，真理长河中有无数礁石险滩。只有不畏攀登的采药者，只有不怕巨浪的弄潮儿，才能登上高峰采得仙草，深入水底觅得骊珠。”