何毓琦的个人博客分享 http://blog.sciencenet.cn/u/何毓琦 哈佛(1961-2001) 清华(2001-date)


On Research and Education (#11) Changing Research Direction and Field of Endeavo 精选

已有 5833 次阅读 2008-4-27 20:31 |系统分类:科研笔记

Many of us got into a particular field of study in science and technology more or less by accident. First of all if you are in high school, you are either immature and hence does not know how to seek advice or lack proper mentor to consult for advice. I remember when I was in high school, the only advice I got was the then conventional Chinese wisdom – i.e., if you are any good in science and mathematics, study engineering but not science such as physics for you will not be able to get a job after graduation.

I decided to choose mechanical engineering. This was because on one occasion when I was about 13, I was able to repair a broken down and rather complex European ornamental clock with a moving and chirping bird mechanism abandoned in our home attic. Without instruction book or working knowledge of any kind I slowly deduced the logic behind the mechanism and to the surprise of everyone made it to work again. So mechanical engineering became my destiny.  When  I applied for college admission, I listed ME as my chosen field. Somehow the admission office of MIT made a mistake and admitted me as a potential electrical engineering major. Actually at that time, ALL entering freshman of MIT study the same set of courses for the first year. You begin to differentiate only in the second year. Students actually decide their course of study at the end of the first year of college. However, since I was officially a potential EE department student, I got invited to many recruiting talks and other events of the EE department. I was a 16 year old alone in the US, there was really no one to advise or mentoring me. So by inertia and ignorance, Electrical Engineering seemed as good as any field to major in. Thus, it became a career choice by default. Similarly my choice for graduate study was not the right decision by hind sight (see my earlier blog article “on Research (#10) http://www.sciencenet.cn/blog/user_content.aspx?id=11577). But in either case, I don’t think they made any long term difference. I am a firm believer that opportunity exist everywhere, so long you practice constant feedback and midcourse correction (see my career advice http://www.sciencenet.cn/blog/user_content.aspx?id=8186) you will come out OK.

The purpose of my telling the above story is to urge young scholar to explore new fields and topics. While it is very comfortable to do incremental research within an established framework, the payoff is far greater in my opinion if you learn to ask the right question in a virgin field of endeavor. I listed the advantages in an earlier blog article. But they are worth repeating it here once more







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 will 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 researh 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.


Thus, it is very beneficial and cost effective to expose yourself to new ways or unfamiliar ways of thinking. Every now and then you should deliberately try to ask new questions in your field or in a new field. The act will help build your self-confidence and chance to make major advances. Of course I am not advocating to abandon a problem at the first sign of difficulty. Good research is hard but pleasurable work. One should have patience and persistence. But don’t get stuck in one frame of mind for too long. My own experience and considered advice – a rough rule of thumb. You should start thinking about changing major research directions in the seventh year and do it every decade. (Note added after posting: It may be well known but just occur to me this is one of the reason academia have sabbaticals every seventh year).


If your are an established scientist, changing field can be painful. In your own field, you already has a reputation. Everyone knows you and respects you. In the new field, you are once more a graduate student and nobody. However, don’t let these temporary discomforts deter you. First of all, it is my firm belief that you can learn any subject sufficient for you to make contributions in six months time. Also you are not encumbered by the established way of thinking in the field. You come in with a fresh viewpoint without being brain-washed as a student by the establishment. This is often a great advantage. In applied field, such as engineering, breadth (i.e. knowing many things well) is as important as depth (knowing only one thing deeply) even if you are an academic.


To all young scholars: good luck and happy journey in your career.


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