Claude Shannon
Up to 100% of the amount of ideas produced, useful good ideas produced by these signals, these are supposed to be arranged in order of increasing ability. At producing ideas, we find a curve something like this. Consider the number of curves produced here - going up to enormous height here.
A very small percentage of the population produces the greatest proportion of the important ideas. This is akin to an idea presented by an English mathematician, Turing, that the human brain is something like a piece of uranium. The human brain, if it is below the critical lap and you shoot one neutron into it, additional more would be produced by impact. It leads to an extremely explosive of the issue, increase the size of the uranium. Turing says this is something like ideas in the human brain. There are some people if you shoot one idea into the brain, you will get a half an idea out. There are other people who are beyond this point at which they produce two ideas for each idea sent in. those are the people beyond the knee of the curve. I don’t want to sound egotistical here, I don’t think that I am beyond the knee of this curve and I don’t know anyone who is. I do know some people that were. I think, for example, that anyone will agree that Isaac Newton would be well on the top of this curve. When you think that at the age of 25 he had produced enough science, physics and mathematics to make 10 or 20 men famous - he produced binomial theorem, differential and integral calculus, laws of gravitation, laws of motion, decomposition of white light, and so on. Now what is it that shoots one up to this part of the curve? What are the basic requirements? I think we could set down three things that are fairly necessary for scientific research or for any sort of inventing or mathematics or physics or anything along that line. I don’t think a person can get along without any one of these three.
The first one is obvious - training and experience. You don’t expect a lawyer, however bright he may be, to give you a new theory of physics these days or mathematics or engineering.
The second thing is a certain amount of intelligence or talent. In other words, you have to have an IQ that is fairly high to do good research work. I don’t think that there is any good engineer or scientist that can get along on an IQ of 100, which is the average for human beings. In other words, he has to have an IQ higher than that. Everyone in this room is considerably above that. This, we might say, is a matter of environment; intelligence is a matter of heredity.
Those two I don’t think are sufficient. I think there is a third constituent here, a third component which is the one that makes an Einstein or an Isaac Newton. For want of a better word, we will call it motivation. In other words, you have to have some kind of a drive, some kind of a desire to find out the answer, a desire to find out what makes things tick. If you don’t have that, you may have all the training and intelligence in the world, you don’t have questions and you won’t just find answers. This is a hard thing to put your finger on. It is a matter of temperament probably; that is, a matter of probably early training, early childhood experiences, whether you will motivate in the direction of scientific research. I think that at a superficial level, it is blended use of several things. This is not any attempt at a deep analysis at all, but my feeling is that a good scientist has a great deal of what we can call curiosity. I won’t go any deeper into it than that. He wants to know the answers. He’s just curious how things tick and he wants to know the answers to questions; and if he sees thinks, he wants to raise questions and he wants to know the answers to those.
Then there’s the idea of dissatisfaction. By this I don’t mean a pessimistic dissatisfaction of the world - we don’t like the way things are - I mean a constructive dissatisfaction. The idea could be expressed in the words, °∞This is OK, but I think things could be done better. I think there is a neater way to do this. I think things could be improved a little. In other words, there is continually a slight irritation when things don’t look quite right; and I think that dissatisfaction in present days is a key driving force in good scientists.
And another thing I°Ød put down here is the pleasure in seeing net results or methods of arriving at results needed, designs of engineers, equipment, and so on. I get a big bang myself out of providing a theorem. If I’ve been trying to prove a mathematical theorem for a week or so and I finally find the solution, I get a big bang out of it. And I get a big kick out of seeing a clever way of doing some engineering problem, a clever design for a circuit which uses a very small amount of equipment and gets apparently a great deal of result out of it. I think so far as motivation is concerned, it is maybe a little like Fats Waller said about swing music - ''either you got it or you ain’t.'' if you ain’t got it, you probably shouldn’t be doing research work if you don’t want to know that kind of answer. Although people without this kind of motivation might be very successful in other fields, the research man should probably have an extremely strong drive to want to find out the answers, so strong a drive that he doesn’t care whether it is 5 o°Øclock - he is willing to work all night to find out the answers and al weekend if necessary. Well now, this is all well and good, but supposing a person has these three properties to a sufficient extent to be useful, are there any tricks, any gimmicks that he can apply to thinking that will actually aid in creative work, in getting the answers in research work, in general, in finding answers to problems? I think there are, and I think they can be catalogued to an certain extent. You can make quite a list of them and I think they would be very useful if one did that, so I am going to give a few of them which I have thought up or which people have suggested to me. And I think if one consciously applied these to various problems you had to solve, in many cases you’d find solutions quicker than you would normally or in cases where you might not find it at all. I thing that good research workers apply these things unconsciously; that is, they do these things automatically and if they were brought forth into the conscious thinking that here’s a situation where I would try this method of approach that would probably get there faster, although I can’t document this statement.
The first one that I might speak of is the idea of simplification. Suppose that you are given a problem to solve, I don’t care what kind of a problem - a machine to design, or a physical theory to develop, or a mathematical theorem to prove, or something of that kind - probably a very powerful approach to this is to attempt to eliminate everything from the problem except the essentials; that is, cut it down to size. Almost every problem that you come across is befuddled with all kinds of extraneous data of one sort or another; and if you can bring this problem down into the main issues, you can see more clearly what you’re trying to do and perhaps find a solution. Now, in so doing, you may have stripped away the problem that you’re after. You may have simplified it to a point that it doesn’t even resemble the problem that you started with; but very often if you can solve this simple problem, you can add refinements to the solution of this until you get back to the solution of the one you started with.
A very similar device is seeking similar known problems. I think I could illustrate this schematically in this way. You have a problem P here and there is a solution S which you do not know yet perhaps over here. If you have experience in the field represented, that you are working in, you may perhaps know of a somewhat similar problem, call it P', which has already been solved and which has a solution, S', all you need to do - all you may have to do is find the analogy from P' here to P and the same analogy from S' to S in order to get back to the solution of the given problem. This is the reason why experience in a field is so important that if you are experienced in a field, you will know thousands of problems that have been solved. Your mental matrix will be filled with P's and S's unconnected here and you can find one which is tolerably close to the P that you are trying to solve and go over to the corresponding S' in order to go back to the S you’re after. It seems to be much easier to make two small jumps than the one big jump in any kind of mental thinking.
Another approach for a given problem is to try to restate it in just as many different forms as you can. Change the words. Change the viewpoint. Look at it from every possible angle. After you’ve done that, you can try to look at it from several angles at the same time and perhaps you can get an insight into the real basic issues of the problem, so that you can correlate the important factors and come out with the solution. It’s difficult really to do this, but it is important that you do. If you don’t, it is very easy to get into ruts of mental thinking. You start with a problem here and you go around a circle here and if you could only get over to this point, perhaps you would see your way clear; but you can’t break loose from certain mental blocks which are holding you in certain ways of looking at a problem. That is the reason why very frequently someone who is quite green to a problem will sometimes come in and look at it and find the solution like that, while you have been laboring for months over it. You’ve got set into some ruts here of mental thinking and someone else comes in and sees it from a fresh viewpoint.
Another mental gimmick for aid in research work, I think, is the idea of generalization. This is very powerful in mathematical research. The typical mathematical theory developed in the following way to prove a very isolated, special result, particular theorem - someone always will come along and start generalization it. He will leave it where it was in two dimensions before he will do it in N dimensions; or if it was in some kind of algebra, he will work in a general algebraic field; if it was in the field of real numbers, he will change it to a general algebraic field or something of that sort. This is actually quite easy to do if you only remember to do it. If the minute you’ve found an answer to something, the next thing to do is to ask yourself if you can generalize this anymore - can I make the same, make a broader statement which includes more - there, I think, in terms of engineering, the same thing should be kept in mind. As you see, if somebody comes along with a clever way of doing something, one should ask oneself °∞Can I apply the same principle in more general ways? Can I use this same clever idea represented here to solve a larger class of problems? Is there any place else that I can use this particular thing?°±
Next one I might mention is the idea of structural analysis of a problem. Suppose you have your problem here and a solution here. You may have two big a jump to take. What you can try to do is to break down that jump into a large number of small jumps. If this were a set of mathematical axioms and this were a theorem or conclusion that you were trying to prove, it might be too much for me try to prove this thing in one fell swoop. But perhaps I can visualize a number of subsidiary theorems or propositions such that if I could prove those, in turn I would eventually arrive at this solution. In other words, I set up some path through this domain with a set of subsidiary solutions, 1, 2, 3, 4, and so on, and attempt to prove this on the basis of that and then this one the basis of these which I have proved until eventually I arrive at the path S. Many proofs in mathematics have been actually found by extremely roundabout processes. A man starts to prove this theorem and he finds that he wanders all over the map. He starts off and prove a good many results which don’t seem to be leading anywhere and then eventually ends up by the back door on the solution of the given problem; and very often when that’s done, when you’ve found your solution, it may be very easy to simplify; that is, to see at one stage that you may have short-cutted across here and you could see that you might have short-cutted across there. The same thing is true in design work. If you can design a way of doing something which is obviously clumsy and cumbersome, uses too much equipment; but after you’ve really got something you can get a grip on, something you can hang on to, you can start cutting out components and seeing some parts were really superfluous. You really didn’t need them in the first place.
Now one other thing I would like to bring out which I run across quite frequently in mathematical work is the idea of inversion of the problem. You are trying to obtain the solution S on the basis of the premises P and then you can’t do it. Well, turn the problem over supposing that S were the given proposition, the given axioms, or the given numbers in the problem and what you are trying to obtain is P. Just imagine that that were the case. Then you will find that it is relatively easy to solve the problem in that direction. You find a fairly direct route. If so, it’s often possible to invent it in small batches. In other words, you’ve got a path marked out here - there you got relays you sent this way. You can see how to invert these things in small stages and perhaps three or four only difficult steps in the proof.
Now I think the same thing can happen in design work. Sometimes I have had the experience of designing computing machines of various sorts in which I wanted to compute certain numbers out of certain given quantities. This happened to be a machine that played the game of nim and it turned out that it seemed to be quite difficult. If took quite a number of relays to do this particular calculation although it could be done. But then I got the idea that if I inverted the problem, it would have been very easy to do - if the given and required results had been interchanged; and that idea led to a way of doing it which was far simpler than the first design. The way of doing it was doing it by feedback; that is, you start with the required result and run it back until - run it through its value until it matches the given input. So the machine itself was worked backward putting range S over the numbers until it had the number that you actually had and, at that point, until it reached the number such that P shows you the correct way. Well, now the solution for this philosophy which is probably very boring to most of you. I’d like now to show you this machine which I brought along and go into one or two of the problems which were connected with the design of that because I think they illustrate some of these things I’ve been talking about. In order to see this, you’ll have to come up around it; so, I wonder whether you will all come up around the table now.
创造性思维
克劳德·香农在贝尔实验室。
1952年3月20日
这些信号所产生的创意数量，乃至其中真正有用的好点子，其产出能力本应被按递增顺序排列。在衡量创意产出时，我们发现了一条大致如此的曲线。请看此处生成的曲线数量——它们在此处攀升至惊人的高度。
只有极少数人贡献了绝大部分的重要思想。这类似于英国数学家图灵提出的一个观点：人脑就像一块铀。人脑如果处于临界质量以下，当你射入一个中子，通过撞击会产生更多中子。这会导致问题的急剧爆发，增大铀的规模。图灵说，这就像人脑中的思想。有些人，如果你向他的大脑输入一个想法，你只能得到半个想法。而另一些人则超越了这一点，他们每接收一个想法，就能产生两个想法。这些人就是超越了曲线拐点的人。我不想显得自大，我不认为我超越了这条曲线的拐点，我也不认识任何这样的人。但我确实认识一些曾经达到这种境界的人。例如，我想任何人都会同意，艾萨克·牛顿会稳稳地位于这条曲线的顶端。想想看，他在25岁时就已经在科学、物理学和数学领域做出了足以让10个或20个人成名的贡献——他提出了二项式定理、微分和积分、万有引力定律、运动定律、白光分解等等。那么，是什么能将一个人推上曲线的这个部分呢？基本要求是什么？我认为我们可以列出三样东西，对于科学研究或任何类型的发明、数学、物理学或类似领域来说，这三样东西是相当必要的。我认为一个人如果缺少这三样中的任何一样，都无法取得成就。
第一个原因显而易见——训练与经验。你不能指望一位律师，无论他多么聪明，能在当下为你提出物理学、数学或工程学的新理论。
第二点是需要具备一定的智力或天赋。换句话说，要做出优秀的研究工作，你的智商必须相当高。我认为，任何优秀的工程师或科学家都无法仅凭100的智商——即人类的平均水平——取得成就。换言之，他必须拥有高于平均水平的智商。在座的各位都远高于这个标准。我们可以说，这是环境因素；而智力则关乎遗传。
我认为那两点还不够。我认为这里还有第三个要素，第三个组成部分，正是它造就了爱因斯坦或艾萨克·牛顿。由于找不到更合适的词，我们姑且称之为“驱动力”。换句话说，你必须要有某种动力，某种渴望去找到答案，渴望去弄清楚事物运作的奥秘。如果没有这种驱动力，即使你拥有世界上所有的训练和才智，你也不会提出问题，自然也就找不到答案。这是一种难以确切描述的特质。它很可能关乎性情；也就是说，很可能关乎早期的训练、童年的经历，这些因素决定了你是否会走上科学研究的道路。我认为在浅层上，它是多种因素的综合作用。这绝非任何深刻的剖析，但我的感觉是，一位优秀的科学家拥有大量我们可以称之为“好奇心”的东西。我不会对此进行更深入的探讨。他想要知道答案。他只是对事物如何运作感到好奇，他想要知道问题的答案；如果他观察到某些现象，他就会提出问题，并想要知道那些问题的答案。
接下来谈谈“不满足感”这个概念。我指的不是那种对世界的悲观不满——觉得现状不如人意——而是一种建设性的不满足感。这种理念可以用这样的话来表达：“这样也行，但我觉得事情可以做得更好。我认为存在更简洁的方法。我觉得还有改进的空间。”换句话说，当事情看起来不够完美时，内心总会持续产生一丝焦躁；我认为在当今时代，这种不满足感正是优秀科学家的核心驱动力。
此外，我还想在此强调，目睹网络成果、实现目标所需的方法、工程师的设计以及设备等带来的乐趣。我自己从提供一个定理中获得极大的满足感。如果我花了一周左右的时间试图证明一个数学定理，最终找到了解决方案，我会从中获得巨大的成就感。看到解决工程问题的巧妙方法，或者设计出一个使用极少设备却能产生显著效果的巧妙电路，也会让我兴奋不已。就动机而言，我认为这或许有点像胖子沃勒对摇摆乐的评价——“要么你有，要么你没有。”如果你没有这种动力，如果你不想知道那种答案，你可能就不应该从事研究工作。尽管缺乏这种动机的人在其他领域可能非常成功，但研究人员很可能应该拥有极其强烈的求知欲，这种欲望如此强烈，以至于他不在乎是否到了下午五点——他愿意通宵工作以找到答案，必要时甚至整个周末都在工作。那么，现在这一切都很好，但假设一个人充分具备这三种特质，足以发挥作用，那么他是否有一些技巧、一些窍门可以应用于思考，从而真正有助于创造性工作、研究工作以及一般问题的解决呢？我认为是有的，而且我认为它们在一定程度上可以被分类。你可以列出一个相当长的清单，我认为如果这样做会非常有用，因此我将提供一些我自己想到的或别人建议给我的方法。我认为，如果有意识地将这些方法应用于你需要解决的各种问题，在许多情况下，你会比平时更快地找到解决方案，或者在原本可能找不到解决方案的情况下找到答案。我认为优秀的研究人员会无意识地运用这些方法；也就是说，他们会自动地做这些事情，如果他们将这种意识带入思考中，意识到在这种情况下可以尝试这种方法，可能会更快地达到目标，尽管我无法为这一说法提供文献支持。
我想谈的第一个理念是简化。 假设你遇到一个需要解决的问题——无论是设计一台机器、发展一套物理理论、证明一个数学定理，还是其他任何类型的问题——一个非常有效的方法，就是尝试剔除问题中所有非本质的东西，也就是将其精简到核心。你遇到的几乎每个问题，都混杂着各种无关的数据；如果你能把问题剥离到主要矛盾，就能更清楚地看到自己要做什么，并可能找到解决方案。在这个过程中，你可能会剥离掉你最初追求的那个问题本身。你可能把它简化到甚至不再像最初问题的地步；但很多时候，如果你能解决这个简化后的问题，你就可以逐步为这个解决方案添加细节，直到它回溯解决你最初的那个问题。
一个非常相似的装置正在寻找相似的已知问题。 我想我可以这样示意性地说明这一点。你这里有一个问题 P，而那边有一个解决方案 S，你可能还不知道它。如果你在相关领域有经验，也就是你正在工作的领域，你或许知道一个有点类似的问题，称之为 P'，它已经被解决并且有一个解决方案 S'。你需要做的——你可能只需要做的——就是找到从 P' 到 P 的类比，以及从 S' 到 S 的相同类比，从而回到给定问题的解决方案。这就是为什么在一个领域的经验如此重要：如果你在一个领域有经验，你会知道成千上万个已经解决的问题。你的思维矩阵将充满互不关联的 P 和 S，你可以找到一个与你试图解决的 P 相当接近的，然后转向对应的 S'，从而回到你追求的 S。在任何类型的思维活动中，进行两次小跳跃似乎比进行一次大跳跃要容易得多。
面对一个既定问题，另一种方法是尽可能多地尝试用不同形式重新表述它。 变换措辞。转换视角。从每一个可能的角度审视它。完成这些之后，你可以尝试同时从多个角度观察，或许就能洞察问题的真正本质，从而关联起重要因素并找到解决方案。真正做到这一点很难，但至关重要。如果不这样做，思维很容易陷入定式。你从这里的问题出发，沿着这个循环打转，如果能跳到这个点，或许就能豁然开朗；但你无法摆脱某些思维定势的束缚，这些定势将你局限在看待问题的特定方式中。这就是为什么一个对该问题完全陌生的人，有时能一眼看穿并轻松找到解决方案，而你却已经为此苦苦钻研了数月。你的思维陷入了某些定式，而别人则以全新的视角来看待它。
我认为，研究工作中另一个有益的心智技巧是"推广"的理念。 这在数学研究中尤为强大。典型的数学理论发展路径往往是：先证明一个非常孤立、特殊的结果或特定定理——随后总会有人开始将其推广。他会从原有的二维情形扩展到N维空间；如果原定理基于某种特定代数结构，他会推广到一般代数域；如果原本限于实数域，他会将其拓展到更一般的代数域或类似范畴。实际上，只要记得去做这件事，推广往往并不困难。当你找到某个问题的答案后，紧接着就该问自己：能否进一步推广？能否提出更广泛的表述来涵盖更多情形？我认为在工程领域也应牢记同样的原则。正如我们所见，当有人提出某种巧妙方法时，我们应该自问："我能否在更广泛的场景中运用相同原理？能否利用这里体现的巧妙思路来解决更广泛类型的问题？这个特定方法还能用在其他什么地方？"
接下来我想提的是问题的结构化分析思路。 假设你的问题在这里，而解决方案在那里。两者之间的跨越可能太大。你可以尝试将这个大的跨越分解为大量的小步骤。如果这是一组数学公理，而这是你试图证明的定理或结论，我可能很难一蹴而就地完成证明。但或许我可以设想一系列辅助定理或命题，只要我能逐一证明它们，最终就能抵达这个解决方案。换句话说，我在这片领域中铺设一条路径，设置一连串的辅助解，步骤1、2、3、4……然后尝试基于前一步证明后一步，如此推进，直到最终走通通往目标S的整条路径。数学中的许多证明实际上正是通过极其迂回的过程发现的。研究者开始证明某个定理时，可能会在思维版图上四处漫游。他出发后证明了许多看似毫无关联的结果，最终却从后门绕回了原问题的解。而且往往在找到解决方案后，简化过程会变得非常容易——你会发现在某个阶段其实可以走捷径，意识到某些环节原本可以跳过。设计工作也是如此。如果你能设计出一种虽然明显笨拙繁琐、使用了过多设备的方法，但一旦你真正掌握了某个可以把握、可以依托的东西，就可以开始削减组件，发现某些部分其实是多余的——它们从一开始就不是必需的。
N 我想指出的另一件事，是我在数学工作中经常遇到的，那就是问题的“逆向思考”。 你试图基于前提 P 来获得解 S，但做不到。那么，不妨把问题反过来：假设 S 是给定的命题、给定的公理，或是题目中给定的数字，而你要设法求得的反而是 P。就想象情况确实如此。然后你会发现，沿着这个方向解决问题会相对容易一些。你会找到一条相当直接的路径。如果这样可行，通常就有可能将其拆解成小步骤来实现。换句话说，你在这里标出了一条路径——那里有你这样设置的继电器。你可以看到如何将这些步骤一小段一小段地逆向操作，也许整个证明中只有三四个比较困难的步骤。
我认为设计工作中也会发生同样的情况。有时我在设计各类计算机器时有过这样的经历：需要根据某些给定量计算出特定数值。碰巧那是一台玩尼姆游戏的机器，结果发现这件事似乎相当困难。虽然能够完成，但完成这个特定计算需要相当多的继电器。但后来我想到，如果我将问题反过来看——假如把给定的条件和要求的结果互换——事情就会变得非常简单；这个想法引导我找到了一种比最初设计简单得多的实现方法。这个方法就是通过反馈来实现：也就是说，你从要求的结果出发，逆向运行直到——让它经过其数值直到与给定的输入匹配。所以机器本身是反向工作的，让范围S遍历数字，直到它得到你实际拥有的数字，在那一刻，直到它达到让P指示出正确路径的那个数字。好吧，这个理念的解决方案对你们大多数人来说可能很无聊。现在我想向你们展示我带来的这台机器，并探讨一两个与设计相关的问题，因为我认为它们能说明我一直在谈论的某些观点。为了看清这个，你们得围过来；所以，我想请你们现在都到桌子这边来。