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)


Why Is Science Conservative? - 科学为何是保守的(一)(原文及译文) 精选

已有 12551 次阅读 2008-6-14 01:07 |系统分类:科研笔记

(NOTES added 6/18/08) I thank  all the readers for their comments and remarks. I am traveling and have no access to Chinese writing hardware. Consequently, I cannot answer in Chinese or correct some minor inaccuracies in the Chinese translation of my article below for now. I intend to supplement this note upon my return.


Conventional wisdom portrays science as innovative (創新) and liberal in thinking in the sense that it is willing to consider all kinds of ideas. But in another sense, science is very conservative. Truly new ideas comes only once in a long while and often after a great deal of struggle for acceptance. This is actually not bad and the way it should be. The world is full of people with or without scientific training who believe they have discovered the truth or invented something remarkable, such as the perpetual motion machine. As a professor at Harvard, I have often received or have letters referred to me written by a person who either

1.       Feels that s/he discovered some new truth but received no support. S/he wants Harvard to look into this injustice, or

2.       S/he has invented a new device that will change the world in revolutionary ways. Would Harvard endorse this device?

Let me say that in my 46 years I have encountered many letters of the above type that are not worth the paper on which they were written. Even well educated people can sometimes delude themselves. As a result science often looks upon any claim of new discovery or breakthrough with a jaundiced eye particularly if such claims come from people one does not know.  Consequently really NEW results often have to face a considerable struggle for acceptance. The history of science has many of such incidents both positive and negative (e.g. the discovery of the pseudo planet PLUTO, and cold fusion results in the 1990s). And if science is under the supervision of politics and too closely tied to economics, then even more abuses can result. I don’t need to repeat well known historical examples. But even if science is free from politics and commerce, new ideas still must struggle to get accepted.

I shall relate a personal experience a generation ago that may be of some value to scholars who are facing similar situations.

First a bit of background. The successes of aerospace control including the moon landing in the 60s are based on modeling dynamic system by nonlinear differential equations and developing a class of control strategies using linearized (perturbed) equations of motion. During the 70s myself and others began to study non differential equation based dynamic systems, e.g. discrete manufacturing processes, communication networks, airport operations, et al. These systems, denoted as discrete event dynamic systems (DEDS), are governed by man-made rules of operation and traditionally belong in the domain of Industrial Engineering  and Operations Research (IEOR). But for me coming from control theory, the natural impulse is to see if we can duplicated our successes in differential equation based dynamic systems for these new DEDS. I also viewed this as an opportunity since researchers in IEOR up to that time  have not emphasized the dynamic aspects of these systems. Lastly, demand for my consulting expertise from industry also were coming from these areas.

Anyhow, my first thought was to see if it was possible to develop some sort of perturbation analysis for the motion of these discrete, nonlinear, discontinuous dynamic systems. The rationale behind this is to develop answer to the question “what will happen to the behavior and hence performance of these DEDS if I make a small perturbation in some design or control parameter of the system.” The significances of such question/answers are obvious. However, strangely enough traditional OR never bothered to ask such a question perhaps thinking that the obvious discontinuous nature of the system behavior renders such question meaningless at the time. The accepted practice is to make two separate experiments or simulations where everything is kept the same except for a small perturbation in the control or design parameter. The difference in observed performances in these two experiments when divided by the small parameter change gives the sensitivity (gradient) of the system performance with respect to the parameter perturbed. If sensitivity for n parameters are desired then n+1 experiments must be performed. The gradient thus calculated is also prone to numerical error and instability due to the fact that you are dividing a generally small and noisy difference by another small number. This is the state of the art when I first announced in 1981 that we have an entirely new way of computing this sensitivity using only ONE simulation experiment regardless how many sensitivities are required. Furthermore, the calculated sensitivity are numerically stable and much more accurate then those computed by differencing method traditionally. The basis of such a claim came from

1.       A real life consulting job starting in 1976 in connection with the manufacturing operations of a well known automobile company

2.       Through extensive simulations, experimental verifications, and intuitive commonsense ideas  we found we could actually accomplish the above claim for this particular manufacturing problem.

3.       I gradually realized that the idea embodied in the solution #2 above can be in fact be generalized to other simulation experiments. During travel in China in the summer of 1981, one afternoon in Wuhan I had an epiphany and came up with a “proof” (rather an intuitive but at the same time analytical understanding) as to why this scheme works in general. Of course by strict mathematical standards, my “proof” was far from rigorous. But it was back up by extensive amount of experimental evidence and is conceptually correct.

Of course to arrive at this point, we already had solved a real problem, accumulated a large amount of experimental evidence, and published a couple of engineering papers in our own field. Given #3 above, I felt I was ready to announce the “breakthrough” to the IEOR world.

The immediate reactions of the IEOR field was

1.       Who is this person we have not heard of before ? (although I was established in my own field, I have not published in the IEOR field nor have I attended their conferences)

2.       This new result cannot possibly be true. Otherwise we would have discovered it long ago. My paper submitted for publication in OR journals was summarily rejected

3.       When I appealed about the rejection, one editor in OR in fact took the trouble of writing to the editor of the control journal where I first published my early results telling the control journal editor that my results were wrong.

4.       Another person in OR took the trouble writing to the National Science Foundation complaining that the government was wasting taxpayers’ money in supporting my research.

If I was not already established and have credibility in my own field, imagine what #3 and #4 above would have done to me even in an environment where no politics nor commerce were involved.

Actually, these struggles were a blessing in disguise. Myself and others who believed in this were forced to come up with a more rigorous proof of the result and actually sharpened the conditions under which the result is mathematically correct and true. Eventually three books and over 1000 published paper came out of this struggle and the sub-discipline of Perturbation Analysis (PA) became established. Professor Xiren Cao of  the Science and Technology University of HongKong is the leading expert on PA and his new book on the subject just came out 2007. I bear no ill feelings towards the field of IEOR and in fact became an accepted member of the field if only grudgingly. I mention this in detail only to illustrate that the conservative nature of science is necessary and not a bad thing  in general. At the same time, my own opinions is to  recommend researchers in general look far and wide in neighboring fields and not spend ones whole career in one sub-discipline. There is much to be said for learning about a new field.


1. 感到他/她们发现的新的真理不被支持,希望哈佛大学能够关注这种不公正。
2. 表示他/她发明了一种新的、能以革命性方式改变世界的设备,希望得到哈佛大学的认可。
1 我从1976年开始就给一家著名汽车公司提供有关制造方面的咨询工作。
2 通过广泛模拟、试验证实,再加上直觉和常识,我们发现我们其实可以满足上述特殊制造问题的需求。
3 我逐渐认识到包含在第2点中的想法可以推而广之到其它模拟试验中去。1981年夏天我在中国旅行的时候,有一天下午在武汉我突然恍然大悟,想明白了怎么能证明这种想法具有普遍性(这其实更像是一种既像直觉又很理性的理解)。当然,如果按照严格的数学标准,我的证据远称不上严格。但广泛的试验证据支持了我的想法,它在概念上是正确的。
1 这个人是谁?我们从没听说过他。(尽管我在自身领域立足已久,但并未在IEOR领域发表过论文,也没有参加过他们的会议。)
2 这一新结果不可能正确,否则应该早就被发现了。我投到作业研究领域期刊上的论文被草草拒绝了。
3 当我对论文被拒提出上诉时,作业研究领域的一位期刊编辑还费尽心机地给那份最发表我论文的控制论杂志的编辑写了封信,告诉他我的结论是错的。
4 另一位作业运筹学研究领域的(可能是审稿人之一)编辑也煞费苦心地写信给NSF,抱怨政府支持我的研究根本就是浪费纳税人的钱。
我说了这么多细节,只是为了举例说明科学上的保守是必需的,这通常并不是一件坏事。同时,我个人的意见是希望研究人员能够把眼光放得远一点,广一点,不妨把目光投向相关的研究领域,而不要把整个研究生涯都花费在某一个学科分支上。关于如何学习和认识一个新领域的问题,我以后要说的还很多。(科学网  任霄鹏译  何姣校 minor revision by YCHo in RED 6.24/08



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