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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)
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.
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.
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"
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".
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.
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
standard.
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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