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

已有 12158 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.

 

传统的认识将科学描绘为思想上的创新和自由,这主要是因为科学乐于考虑所有的想法和观点。但在另一种意义上,科学是非常保守的。真正新颖的认识只会偶尔出现,而要被人们接受往往还要经过大量的努力和斗争。事实上,这并不是坏事,而是科学应有的方式。
 
世界上到处都有这样的人,不论是否受过科学训练,他们都认为自己发现了真理或者做出了非凡的发明,比如永动机。作为哈佛大学的教授,我经常能收到或者得到别人转来的这种信,写这些信的人:
 
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。
 
我要说的是,在我46年的学术生涯中,我收到许多这样的信,来信的内容还没有写这些内容的信纸有价值。即使是受到良好教育的人,有时也会自我蒙蔽、自我迷惑。结果就是,科学往往以带有偏见、敌视的眼光看待任何所谓的新发现、新进展,尤其是当它们来自于默默无名的小人物的时候。相应地,真正的结果往往必须经过相当大的努力和斗争,才能为人接受。科学史上不乏这样的例子,正面和负面的都有,(比如发现冥王星是伪行星以及20世纪90年代的冷聚变理论等。)同时,如果科学被置于政治的监管之下,并与经济的关系过于紧密,那么就会产生更多的问题。我无需重提那些历史上著名的例子了,但需要强调的是,即使科学免于政治和商业的影响,新的认识要想被人接受必须经过不懈的努力。
 
接下来,我将讲述几十年前的一段个人经历,这或许对处在类似情形的学者们有些价值。我先介绍一下当时的背景。航天控制的成功包括7060年代的月球着陆等,都是基于利用非线性微分方程建模动态系统,并利用运动的线性化(扰动)方程发展出一类控制策略。在20世纪80年代,我和其他一些人开始研究基于非微分方程的动态系统,比如离散制造过程、通讯网络、机场操作等。这些被称为离散事件动态系统DEDS)的系统由人为的操作规则控制,传统上属于工业工程和作业运筹学研究(IEOR)领域。但由于我的出身是控制论,自然就是想看看我们在基于微分方程的动态系统上的成功能否应用于这些新的DEDS。我也将这看作一次机遇,因为IEOR方面的研究人员那时仍未重点开展这些系统的动态方面的研究。此外,工业界也开始要求我提供这些领域的咨询意见。
 
总之,我最初的想法就是要看看有没有可能就离散、非线性、不连续的动态系统,发展出某种扰动(摄动)分析。其中的基本原理就是要找到下述问题的答案,即如果我在DEDS的参量设计或控制做一个小的干扰,那么这些系统的行为和表现将会发生什么变化?这个问题的重要性是不言而喻的。然而,奇怪的是传统的作业运筹学研究(OR)从未提出这样问题,或许是考虑到当时系统明显的不连续性会让这种问题毫无意义。通行的做法是进行两次单独的试验或者模拟,其他一切条件都是相同的,只有控制或设计参量上的微扰不同。用两次试验观察到的系统表现差异除以微小的参量变化,就得出了系统表现对于干扰参量的敏感度(斜率)。如果要得到系统对于n个参量的敏感度,就需要进行n+1次试验。而且由于用一个很小的数字去除另一个通常较小且伴有噪声的数字,计算出的斜率容易产生数值误差,而且不太稳定。这就是我在1981年首次宣称发现了一种全新方法时的情况。使用我的新方法,不管干扰参量有多少,需要计算多少个敏感度,敏感度的计算均可在一次模拟试验中完成。此外,新方法计算出的敏感度在数值上是稳定的,而且比传统的差分方法精确得多。我的这种理论基础是:
 
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。
 
当然在到达这一步之前,我们已经解决了一个现实中的问题,积累了大量的试验证据,并且发表了数篇这个领域的工程学论文。有了上述第3点作为前提,我觉得我准备好向IEOR界宣布这一突破了。
 
IEOR领域马上就做出了反应:
 
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。
 
要不是我在自己的领域里已经有了一定的名气和公信力,想象一下上述第3点和第4点会对我造成什么影响,即使是在没有政治或者商业介入的环境中。
 
事实上,这些困难和斗争是因祸得福,因为我自己和其他坚信这一结果的人都不得不寻求更加严格的证明,并且不断提炼在什么样的条件下该结论在数学上既合理又正确。最终,在这番斗争中诞生了3本书和1000多篇论文,扰动分析(PA)的一个学科分支诞生了。香港科技大学的曹希仁教授是PA领域的顶尖专家,他在这一学科上的新书于2007年面世。而我再也不讨厌IEOR领域了,事实上我终于被该领域接纳,成为了其中一员,尽管他们对有些不太情愿。
 
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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