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How to do research

已有 34882 次阅读 2007-5-19 04:59 |系统分类:科研笔记

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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.

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 .

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

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:

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)


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


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.

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


ii.Technology issues.  What we see coming up that will change the control


iii.Computational tools.

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:






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.

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 ain'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.

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".


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.

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.

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.

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.

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 (冈门造车)" 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.

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.

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


In  short, there is no royal road to research success except focused hard work.

Note added 5/11/2106: There is a nice Chinese summary of this and related article at http://blog.sciencenet.cn/home.php?mod=space&uid=535297&do=blog&id=636074  何毓琦院士教年轻人如何做科研 精选


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