>>>  新興科技、社會發展等人文科學探討  >>>

簡體     傳統

你和你的研究，理查德·汉明 （Richard Hamming）

理查德·汉明（Richard Hamming）在1986年3月发表了这次演讲。[1] 这是我读过的最好的演讲之一，长期以来一直影响着我对如何度过时间的看法。

这个周末，我向一些人提到了它，令我惊讶的是，他们从未听说过它。所以我虽然我会在这里分享它：

[23 年 5 月 28 日补充：请参阅 Gwern 的这个很棒的注释版本。

很高兴来到这里。我怀疑我是否能不辜负介绍。我演讲的题目是“你和你的研究”。这不是关于管理研究，而是关于你个人如何进行研究。我可以就另一个主题发表演讲——但不是，而是关于你。我不是在谈论普通的普通研究;我说的是伟大的研究。为了描述伟大的研究，我偶尔会说诺贝尔奖类型的工作。它不一定要获得诺贝尔奖，但我指的是那些我们认为是重要的事情。相对论，如果你愿意的话，香农的信息论，任何数量的杰出理论——这就是我正在谈论的那种东西。

现在，我是怎么开始做这项研究的？在洛斯阿拉莫斯，我被请来运行其他人已经开始使用的计算机，这样那些科学家和物理学家就可以重新开始工作。我看到我是个傀儡。我看到，虽然身体上是一样的，但他们是不同的。说白了，我很羡慕。我想知道为什么他们与我如此不同。我近距离地看到了费曼。我看到了费米和泰勒。我看到了奥本海默。我见到了汉斯·贝特：他是我的老板。我见过不少非常有能力的人。我开始对那些这样做的人和那些可能已经这样做的人之间的区别非常感兴趣。

当我来到贝尔实验室时，我进入了一个非常高效的部门。博德当时是部门负责人;香农在那里，还有其他人。我继续研究这些问题，“为什么？”和“有什么区别？”。随后，我继续阅读传记、自传，问人们一些问题，比如：“你是怎么来的？我试图找出有什么区别。这就是这次演讲的意义所在。

那么，为什么这次演讲很重要呢？我认为这很重要，因为据我所知，你们每个人都有一次生命。即使你相信轮回，它对你从一世到下一世也没有任何好处！为什么你不应该在这一生中做有意义的事情，无论你如何定义重要？我不打算定义它——你知道我的意思。我将主要谈论科学，因为这是我所研究的。但据我所知，其他人也告诉我，我所说的大部分内容适用于许多领域。在大多数领域，杰出的工作都具有非常相似的特征，但我将自己局限于科学。

为了单独了解你，我必须用第一人称说话。我必须让你放下谦虚，对自己说，'是的，我想做一流的工作。我们的社会对那些真正致力于做好工作的人不屑一顾。你不应该这样做;运气应该降临在你身上，你偶然做伟大的事情。嗯，这有点傻。我说，你为什么不着手做一些有意义的事情。你不必告诉别人，但你不应该对自己说，“是的，我想做一些有意义的事情。

为了进入第二阶段，我必须放下谦虚，用第一人称谈论我所看到的，我做了什么，我听到了什么。我要谈谈一些人，其中一些你认识，我相信当我们离开时，你不会引用我说的一些话。

让我不是从逻辑上开始，而是从心理上开始。我发现主要的反对意见是，人们认为伟大的科学是靠运气完成的。这完全是运气问题。好吧，考虑一下爱因斯坦。注意他做了多少不同的事情是好的。都是运气吗？是不是有点太重复了？以香农为例。他不只是做信息论。几年前，他做了一些其他的好事，还有一些仍然被锁在密码学的安全性中。他做了很多好事。

你一次又一次地看到，一个好人不仅仅是一件事。偶尔一个人一生只做一件事，我们稍后会谈到，但很多时候是重复的。我声称运气不会涵盖一切。我要引用巴斯德的一句话，“运气眷顾有准备的头脑。我认为这和我所相信的一样。确实有运气的成分，不，没有。有准备的头脑迟早会发现一些重要的事情并去做。所以是的，这是运气。你做的特别的事情是运气，但你做某事不是。

例如，当我来到贝尔实验室时，我和香农共用一个办公室一段时间。与此同时，他在做信息论，我在做编码理论。令人怀疑的是，我们两个人在同一地点同时做到了——那是在大气层中。你可以说，'是的，这是运气。另一方面，你可以说，“但是为什么贝尔实验室的所有人中只有两个人这样做了呢？是的，部分是运气，部分是有准备的头脑;但“部分”是我要谈论的另一件事。所以，虽然我会再来几次运气，但我想把运气这个问题作为你是否做得好的唯一标准。我声称你对它有一些控制权，但不是完全控制。最后，我将引用牛顿关于这个问题的话。牛顿说：“如果其他人能像我一样努力思考，那么他们也会得到类似的结果。

你所看到的一个特征，包括伟大的科学家在内的许多人都有，是通常在他们年轻的时候，他们有独立的思想，并有勇气去追求它们。例如，爱因斯坦在12或14岁左右的时候问自己一个问题，“如果我用光速去看光波，它会是什么样子？现在他知道电磁理论说你不能有一个平稳的局部最大值。但是，如果他随着光速移动，他会看到一个局部最大值。他在12岁、14岁或那里的某个地方看到了一个矛盾，一切都不对劲，光速有一些特殊的东西。他最终创造了狭义相对论是幸运吗？在早期，他通过思考碎片来奠定一些碎片。这是必要条件，但不是充分条件。我要谈的所有这些项目都是运气而不是运气。

拥有大量的“大脑”怎么样？听起来不错。在座的大多数人可能有足够的大脑来做一流的工作。但伟大的工作不仅仅是大脑。大脑的测量方式多种多样。在数学、理论物理学、天体物理学中，通常大脑在很大程度上与操纵符号的能力相关。因此，典型的智商测试很容易给他们打得相当高。另一方面，在其他领域，情况就不同了。例如，比尔·普凡（Bill Pfann），那个做区域融化的人，有一天来到我的办公室。他脑海中模糊地有这个想法，关于他想要什么，他有一些方程式。我很清楚，这个人不太懂数学，而且他不太善于表达。他的问题似乎很有趣，所以我把它带回家做了一点工作。最后，我向他展示了如何运行计算机，这样他就可以计算自己的答案。我给了他计算的能力。他继续前进，得到了自己部门的认可，但最终他获得了该领域的所有奖项。一旦他开始了良好的工作，他的害羞、笨拙、口齿不清就消失了，他在许多其他方面都变得更有效率了。当然，他变得更加善于表达。

我可以用同样的方式引用另一个人。我相信他不在观众席上，即一个名叫克洛斯顿的家伙。我在约翰·皮尔斯（John Pierce）的团队中处理一个问题时遇到了他，我认为他没有太多。我问在学校里和他一起上学的朋友，“他在研究生院是这样的吗？ ”是的，“他们回答说。好吧，我本来会解雇这个家伙的，但 J. R. Pierce 很聪明，让他继续留任。Clogston 终于完成了 Clogston 电缆。在那之后，有源源不断的好主意。一次成功给他带来了信心和勇气。

成功科学家的特征之一是有勇气。一旦你鼓起勇气，相信你可以做重要的问题，那么你就可以了。如果你认为你做不到，几乎可以肯定你不会。勇气是香农最常拥有的东西之一。你只需要想想他的大定理。他想创建一种编码方法，但他不知道该怎么做，所以他做了一个随机代码。然后他被卡住了。然后他问了一个不可能的问题，“平均随机码会做什么？然后，他证明了平均代码是任意好的，因此必须至少有一个好的代码。除了一个有无限勇气的人，谁敢去想这些想法呢？这是伟大科学家的特征;他们有勇气。他们将在不可思议的情况下继续前进;他们思考并继续思考。

年龄是物理学家特别担心的另一个因素。他们总是说，你必须在年轻的时候这样做，否则你永远不会这样做。爱因斯坦很早就做了一些事情，所有的量子力学研究员在做最好的工作时都年轻得令人作呕。大多数数学家、理论物理学家和天体物理学家在年轻时都会做我们认为最好的工作。不是他们晚年不做好事，而是我们最看重的往往是他们早年做的事。另一方面，在音乐、政治和文学方面，我们认为他们最好的作品往往完成得很晚。我不知道你所处的哪个领域如何符合这个规模，但年龄有一些影响。

但让我说一下为什么年龄似乎有它的影响。首先，如果你做了一些好的工作，你会发现自己在各种委员会中，无法再做任何工作。你可能会发现自己就像我看到布拉坦获得诺贝尔奖时一样。宣布获奖的那天，我们都聚集在阿诺德礼堂;三位获奖者都起身致辞。第三位是布拉坦，他几乎眼里含着泪水，他说：“我知道诺贝尔奖的影响，我不会让它影响我;我将保持老沃尔特·布拉坦（Walter Brattain）的好状态。我对自己说，'那很好。但几周后，我发现它正在影响他。现在他只能解决大问题。

当你出名时，很难解决小问题。这就是香农的所作所为。在信息论之后，你为安可做什么？伟大的科学家经常犯这个错误。他们未能继续种植小橡子，强大的橡树就是从这些橡子中生长出来的。他们试图把大事搞定。但事实并非如此。所以这就是为什么你发现当你得到早期认可时，它似乎会让你绝育的另一个原因。事实上，我会给你多年来我最喜欢的一句话。在我看来，普林斯顿高等研究院毁掉的优秀科学家比任何机构创造的都多，根据他们来之前做了什么来判断，根据他们来之后做了什么来判断。并不是说他们后来不好，而是他们在到达那里之前是一流的，只有在他们之后才很好。

这带来了一个话题，也许是无序的，工作条件。大多数人认为最好的工作条件，其实并非如此。很明显，它们不是因为人们在工作条件恶劣时往往最有生产力。剑桥物理实验室最好的时代之一就是他们几乎拥有棚屋的时候——他们做了一些有史以来最好的物理学。

我给你讲一个我自己私生活的故事。在早期，我就清楚地意识到，贝尔实验室不会给我传统的编程人员，让我以绝对二进制的方式对计算机进行编程。很明显，他们不会这样做。但每个人都是这样做的。我可以毫不费力地去西海岸，在飞机公司找到一份工作，但令人兴奋的人在贝尔实验室，而飞机公司的人却没有。我想了很久，“我是否想去？”我想知道我怎样才能从两个可能的世界中获得最好的结果。我最后对自己说，'汉明，你认为机器几乎可以做任何事情。为什么你不能让他们写程序呢？起初在我看来是一个缺陷，迫使我很早就开始自动编程。看似错误的东西，通常，通过观点的改变，被证明是你能拥有的最大资产之一。但是，当你第一次看到这个东西时，你不太可能认为，“哎呀，我永远不会得到足够的程序员，所以我怎么能做任何伟大的编程呢？

还有许多其他同类故事;格蕾丝·霍珀（Grace Hopper）也有类似的。我认为，如果你仔细观察，你会发现，伟大的科学家往往通过把问题转过来，把一个缺陷变成了一个资产。例如，许多科学家在发现自己做不到一个问题时，最终开始研究为什么不做。然后他们把它反过来说，“当然，这就是它”，并得到了一个重要的结果。所以理想的工作条件很奇怪。你想要的并不总是最适合你的。

现在是驱动问题。你观察到，大多数伟大的科学家都有巨大的动力。我在贝尔实验室与约翰·图基（John Tukey）共事了十年。他有巨大的动力。在我加入大约三四年后的一天，我发现约翰·图基比我年轻一点。约翰是个天才，而我显然不是。我冲进博德的办公室，问道，“我这个年纪的人怎么能像约翰·图基那样知道那么多呢？他靠在椅子上，双手放在脑后，微微一笑，说：“你会惊讶的，汉明，如果你像他那样努力工作那么多年，你会知道多少。我只是溜出办公室！

博德的意思是：“知识和生产力就像复利。假设两个能力大致相同的人，一个人的工作量比另一个人多百分之十，后者的产量将比前者高出两倍以上。你知道的越多，你学到的就越多;你学得越多，你能做的就越多;你能做的越多，机会就越多——这很像复利。我不想给你一个费率，但这是一个非常高的费率。如果两个人的能力完全相同，那么一个日复一日地管理以多思考一个小时的人将在一生中大大提高工作效率。我把博德的话记在心里;几年来，我花了很多时间试图更努力地工作，我发现，事实上，我可以完成更多的工作。我不喜欢在我妻子面前说这句话，但有时我确实有点忽视了她;我需要学习。如果你打算完成你想做的事情，你必须忽略一些事情。这是毫无疑问的。

关于驱动力，爱迪生说：“天才是99%的汗水和1%的灵感。他可能夸大其词，但这个想法是，扎实的工作，稳步应用，会让你出人意料地走得更远。稳步应用的努力，多做一点工作，智能应用是什么。这就是问题所在;驱动器，误用，不会带你到任何地方。我经常在想，为什么我在贝尔实验室的那么多好朋友，他们和我一样努力工作，却没有那么多东西可以展示。努力的误用是一个非常严重的问题。仅仅努力工作是不够的——它必须明智地应用。

我想谈谈另一个特点;这种特质就是模棱两可。我花了一段时间才发现它的重要性。大多数人喜欢相信某事是真的，也可能不是真的。伟大的科学家可以很好地容忍模棱两可。他们相信这个理论足以继续前进;他们对此表示怀疑，以至于注意到了错误和故障，因此他们可以挺身而出，创造新的替代理论。如果你相信太多，你永远不会注意到缺陷;如果你怀疑太多，你就不会开始。它需要一个可爱的平衡。但大多数伟大的科学家都非常清楚为什么他们的理论是正确的，他们也很清楚一些不太合适的轻微不合，他们不会忘记它。达尔文在他的自传中写道，他发现有必要写下每一条似乎与他的信念相矛盾的证据，否则它们就会从他的脑海中消失。当你发现明显的缺陷时，你必须保持敏感并跟踪这些事情，并密切关注如何解释它们或如何改变理论以适应它们。这些往往是伟大的贡献。伟大的贡献很少是通过添加另一个小数位来完成的。归根结底是一种情感承诺。大多数伟大的科学家都完全致力于解决他们的问题。那些不敬业的人很少能做出杰出的、一流的工作。

再说一遍，情感上的投入是不够的。这显然是一个必要条件。我想我可以告诉你原因。每个研究过创造力的人最终都会说，“创造力来自你的潜意识。不知何故，突然间，它就在那里。它只是出现。好吧，我们对潜意识知之甚少;但有一件事你很清楚，你的梦想也来自你的潜意识。而且你也知道，在相当程度上，你的梦想是对当天经历的改造。如果你日复一日地深深地沉浸在一个话题中，你的潜意识除了解决你的问题之外别无他法。所以你在某个早晨醒来，或者某个下午醒来，答案就有了。对于那些不致力于解决当前问题的人来说，潜意识会在其他事情上犯错，不会产生大的结果。因此，管理自己的方法是，当你遇到一个真正重要的问题时，不要让其他任何事情成为你关注的中心——你把你的想法放在这个问题上。让你的潜意识保持饥饿，这样它就必须解决你的问题，这样你就可以安然入睡，并在早上免费获得答案。

Alan Chynoweth提到我曾经在物理桌上吃饭。我和数学家们一起吃饭，我发现我已经知道相当多的数学知识了;事实上，我并没有学到太多东西。正如他所说，物理表是一个令人兴奋的地方，但我认为他夸大了我的贡献。听 Shockley、Brattain、Bardeen、JB Johnson、Ken McKay 和其他人的演讲非常有趣，我学到了很多东西。但不幸的是，诺贝尔奖来了，晋升来了，剩下的就是渣滓。没有人想要剩下的东西。好吧，和他们一起吃饭是没有用的！

在食堂的另一边是一张化学桌。我曾与其中一位研究员戴夫·麦考尔（Dave McCall）共事过;此外，他当时正在向我们的秘书求爱。我走过去说，'你介意我加入你吗？他们不能拒绝，所以我开始和他们一起吃了一段时间。我开始问，''你所在领域的重要问题是什么？大约一周后，“你在处理什么重要的问题？又过了一段时间，有一天我进来说，'如果你正在做的事情不重要，如果你认为它不会导致一些重要的事情，你为什么要在贝尔实验室工作呢？在那之后，我不受欢迎;我得找别人一起吃饭！那是在春天。

秋天，戴夫·麦考尔（Dave McCall）在大厅里拦住了我，说：“汉明，你的那句话深深地打动了我的皮肤。我整个夏天都在思考这个问题，即我所在领域的重要问题是什么。我没有改变我的研究，“他说，”但我认为这是非常值得的。我说，'谢谢你，戴夫，'然后继续说。几个月后，我注意到他被任命为部门负责人。前几天我注意到他是美国国家工程院院士。我注意到他成功了。我从未听说过在科学界和科学界提到那张桌子上任何其他研究员的名字。他们无法问自己，“我所在领域的重要问题是什么？

如果你不处理一个重要的问题，你就不太可能做重要的工作。这是显而易见的。伟大的科学家已经仔细地思考了他们领域中的一些重要问题，他们一直在思考如何解决这些问题。让我警告你，“重要问题”必须谨慎措辞。从某种意义上说，物理学中的三个悬而未决的问题，是我在贝尔实验室工作时从未研究过的。我的意思是保证获得诺贝尔奖和您想提及的任何金额。我们没有研究（1）时间旅行，（2）瞬移，（3）反重力。它们不是重要的问题，因为我们没有攻击。使问题变得重要的不是结果，而是你有一个合理的攻击。这就是问题的重要性所在。当我说大多数科学家不研究重要问题时，我的意思是在这个意义上。据我所知，一般的科学家几乎把所有的时间都花在了他认为不重要的问题上，他也不相信这些问题会导致重要的问题。

我之前说过种植橡子，这样橡树就会生长。你不能总是确切地知道去哪里，但你可以在可能发生某些事情的地方保持活跃。即使你相信伟大的科学是运气问题，你也可以站在闪电击中的山顶上;你不必躲在你安全的山谷里。但是普通的科学家几乎一直在做例行的安全工作，所以他（或她）的产量并不高。就是这么简单。如果你想把工作做好，你显然必须在重要的问题上下功夫，你应该有一个想法。

在约翰·图基（John Tukey）和其他人的敦促下，我终于采用了我称之为“伟大思想时间”（Great Thoughts Time）的方法。当我星期五中午去吃午饭时，我只会在那之后讨论伟大的想法。我所说的伟大想法是指：“计算机在整个AT&T中扮演什么角色？”、“计算机将如何改变科学？””例如，我当时得出的结论是，十分之九的实验是在实验室完成的，十分之一的实验是在计算机上完成的。有一次，我对副总统们说，这将是相反的，即十分之九的实验将在计算机上完成，十分之一的实验将在实验室中完成。他们知道我是一个疯狂的数学家，没有现实感。我知道他们错了，他们被证明是错的，而我被证明是对的。当他们不需要实验室时，他们就会建造实验室。我看到计算机正在改变科学，因为我花了很多时间问“计算机将对科学产生什么影响，我该如何改变它？我问自己，''它将如何改变贝尔实验室？我曾经在同一次演讲中说过，在我离开之前，贝尔实验室超过一半的人将与计算机密切互动。好吧，你们现在都有终端了。我认真思考我的领域将走向何方，机会在哪里，以及要做的事情是什么。让我去那里，这样我就有机会做一些重要的事情。

大多数伟大的科学家都知道许多重要的问题。他们有 10 到 20 个重要问题，他们正在寻找攻击。当他们看到一个新想法出现时，人们会听到他们说：“嗯，这与这个问题有关。他们放下所有其他东西并追逐它。现在我可以告诉你一个告诉我的恐怖故事，但我不能保证它的真实性。我坐在机场里和我一个来自洛斯阿拉莫斯的朋友聊天，说裂变实验在欧洲发生是多么幸运，因为这让我们在美国的原子弹上工作。他说：''不;在伯克利，我们收集了一堆数据;我们没有办法减少它，因为我们正在建造更多的设备，但如果我们减少这些数据，我们就会发现裂变。他们手里拿着它，他们没有追求它。他们排在第二位！

伟大的科学家，当机会出现时，他们会去追求它，并追求它。他们放弃了所有其他东西。他们摆脱了其他东西，他们追求一个想法，因为他们已经把事情想清楚了。他们的思想已经准备好了;他们看到了机会，并去追逐它。当然，很多时候它并不奏效，但你不必击中他们中的许多人来做一些伟大的科学研究。这很容易。主要技巧之一就是长寿！

另一个特征，我花了一段时间才注意到。我注意到以下关于在门打开或关门的情况下工作的人的事实。我注意到，如果你把办公室的门关上，你今天和明天就能完成更多的工作，而且你的工作效率比大多数人都高。但 10 年后，不知何故，你不知道什么问题值得努力;你所做的所有辛勤工作在重要性上都是无关紧要的。开着门工作的人会受到各种干扰，但他偶尔也会得到关于世界是什么以及什么是重要的线索。现在我无法证明因果顺序，因为你可能会说，「关闭的门象徵着一个关闭的心灵。我不知道。但我可以说，那些敞开大门工作的人和那些最终做重要事情的人之间有很好的相关性，尽管那些关着门工作的人往往更努力地工作。不知何故，他们似乎在做一件稍微错误的事情——不多，但足以让他们错过名声。

我想谈谈另一个话题。它基于我想你们很多人都知道的那首歌，“这不是你做什么，而是你做的方式。我将从我自己的例子开始。在绝对二进制的日子里，我被骗到在数字计算机上做，这是最好的模拟计算机无法解决的问题。我得到了答案。当我仔细想了想，对自己说，'你知道，汉明，你将不得不提交一份关于这项军事工作的报告;在你花了很多钱之后，你将不得不考虑它，每个模拟安装都会希望报告看看他们是否找不到其中的缺陷。至少可以说，我正在用一种相当糟糕的方法进行所需的集成，但我得到了答案。我意识到，事实上，问题不仅仅是得到答案;这是第一次，毫无疑问，我可以用数字机器在自己的地面上击败模拟计算机。我重新设计了求解方法，创造了一个漂亮而优雅的理论，并改变了我们计算答案的方式;结果没有什么不同。发表的报告有一种优雅的方法，后来被称为“汉明积分微分方程的方法”。它现在有点过时了，但有一段时间它是一种非常好的方法。通过稍微改变问题，我做了重要的工作，而不是琐碎的工作。

同样，早期在阁楼上使用机器时，我正在解决一个又一个问题;相当多的人是成功的，也有一些失败。一个星期五，我做完一道题后回家了，奇怪的是，我并不开心;我很郁闷。我可以看到生活是一个接一个问题的长序列。经过一段时间的思考，我决定，“不，我应该大规模生产可变产品。我应该关心明年的所有问题，而不仅仅是我面前的问题。通过改变问题，我仍然得到了同样或更好的结果，但我改变了事情并做了重要的工作。我解决了一个主要问题——当我不知道它们会是什么时，我如何征服机器并解决明年的所有问题？我该如何准备？我该怎么做才能掌握它？我如何遵守牛顿法则？他说：“如果我比别人看得更远，那是因为我站在巨人的肩膀上。这些天我们站在彼此的脚上！

你应该以这样一种方式做你的工作，让其他人可以在它的基础上建立起来，所以他们确实会说，“是的，我站在某某的肩膀上，我看得更远。科学的本质是累积的。通过稍微改变一个问题，你通常可以做伟大的工作，而不仅仅是好的工作。我没有攻击孤立的问题，而是下定决心，我永远不会再解决孤立的问题，除非作为类的特征。

现在，如果你是一个数学家，你就会知道，推广的努力通常意味着解决方案很简单。经常停下来说，“这是他想要的问题，但这是某某的特征。是的，我可以用比特定方法优越得多的方法攻击整个班级，因为我之前被嵌入了不必要的细节。抽象业务经常使事情变得简单。此外，我把方法归档，为未来的问题做好准备。

在结束这一部分时，我会提醒你，“这是一个可怜的工人责怪他的工具——好人继续工作，考虑到他所拥有的，并得到他所能得到的最好的答案。我建议，通过改变问题，通过以不同的方式看待事物，你可以对你的最终生产力产生很大的影响，因为你可以以这样一种方式去做，人们确实可以在你做过的事情上再接再厉，或者你可以用这样一种方式去做，让下一个人不得不再次复制你做过的事情。这不仅仅是工作的问题，而是你写报告的方式，你写论文的方式，整个态度。做一个广泛的、一般的工作，就像做一个非常特殊的案例一样容易。而且它更令人满意和有益！

我现在来谈谈一个非常令人反感的话题;仅仅做一份工作是不够的，你必须卖掉它。“推销”给科学家是一件尴尬的事情。它非常丑陋;你不应该这样做。世界应该在等待，当你做一些伟大的事情时，他们应该冲出来欢迎它。但事实是，每个人都忙于自己的工作。你必须把它呈现得如此之好，以至于他们会把他们正在做的事情放在一边，看看你做了什么，读一读，然后回来说，“是的，这很好。我建议，当你打开一本日记时，当你翻页时，你会问为什么你读一些文章而不是其他文章。你最好写你的报告，这样当它发表在《物理评论》上时，或者你想要的任何地方，当读者翻页时，他们不仅会翻你的页面，而且会停下来阅读你的页面。如果他们不停下来阅读它，你就不会得到学分。

在销售中，您必须做三件事。你必须学会写得清楚好，这样人们才能读懂它，你必须学会进行合理的正式演讲，你还必须学会进行非正式的演讲。我们有很多所谓的“幕后科学家”。在会议上，他们会保持沉默。三周后，在做出决定后，他们提交了一份报告，说明你为什么要这样做。好吧，为时已晚。他们不会在激烈的会议中，在活动的中间站起来说，“出于这些原因，我们应该这样做。你需要掌握这种沟通形式以及准备好的演讲。

刚开始演讲时，我的身体几乎生病了，我非常非常紧张。我意识到我要么必须学会顺利发表演讲，否则我基本上会部分瘫痪我的整个职业生涯。有一天晚上，IBM第一次邀请我在纽约发表演讲，我决定要做一个非常好的演讲，一个需要的演讲，不是技术性的演讲，而是广泛的演讲，最后如果他们喜欢，我会悄悄地说，“只要你想要一个，我就会进来给你一个。结果，我得到了大量的练习，向有限的听众发表演讲，我克服了害怕。此外，我还可以研究哪些方法是有效的，哪些是无效的。

在参加会议时，我已经在研究为什么有些论文被记住了，而大多数论文却没有被记住。技术人员想做一个非常有限的技术演讲。大多数时候，听众想要一个广泛的一般性演讲，并且想要比演讲者愿意提供的更多的调查和背景。结果，许多谈判都是无效的。演讲者说出一个主题，然后突然投入到他所解决的细节中。观众中很少有人会跟随。你应该画一幅大致的图景，说明为什么它很重要，然后慢慢地给出一个草图。然后更多的人会说，“是的，乔做到了，”或者“玛丽做到了;我真的看到它在哪里;是的，玛丽真的讲得很好;我明白玛丽的所作所为。倾向于进行高度限制的、安全的谈话;这通常是无效的。此外，许多演讲都充满了太多的信息。所以我说这种销售的想法是显而易见的。

让我总结一下。你必须解决重要的问题。我否认这都是运气，但我承认运气是有相当的成分。我同意巴斯德的“运气眷顾有准备的头脑”。我非常喜欢我所做的事情。多年来，周五下午——只有伟大的想法——意味着我花了 10% 的时间试图理解该领域更大的问题，即什么是重要的，什么是不重要的。我发现在早期，我一直相信“这个”，但花了整整一周的时间朝着“那个”方向前进。这有点愚蠢。如果我真的相信行动已经结束了，我为什么要朝这个方向前进？我要么改变我的目标，要么改变我所做的事情。所以我改变了我所做的一些事情，我朝着我认为重要的方向前进。就这么简单。

现在你可能会告诉我，你无法控制你必须做什么。好吧，当你第一次开始时，你可能不会。但是，一旦你取得了适度的成功，就会有更多的人要求结果，而不是你所能提供的，你有一些选择的权力，但不是完全的。我给你讲一个关于这个故事的故事，它与教育你的老板有关。我有一个名叫谢尔库诺夫的老板;他曾经是，现在仍然是我的一个非常好的朋友。一些军人来找我，要求在星期五之前给出一些答案。好吧，我已经将我的计算资源用于为一群科学家即时减少数据;我陷入了简短、小而重要的问题。这位军人希望我在周五结束前解决他的问题。我说，'不，我星期一给你。我可以在周末工作。我现在不打算这样做了。他去找我的老板谢尔库诺夫，谢尔库诺夫说，'你必须为他管理这个;他必须在周五之前拿到它。我告诉他，''我为什么要这样做？他说，“你必须这样做。我说，“好吧，谢尔盖，但是你星期五下午坐在办公室里，赶上回家的晚班车，看着这个家伙走出那扇门。星期五下午晚些时候，我给了军人答案。然后我去了谢尔库诺夫的办公室坐了下来;当那人出去时，我说，'你看谢尔库诺夫，这家伙的胳膊下什么都没有;但我给了他答案。星期一早上，谢尔库诺夫打电话给他，说：“你周末来上班了吗？我能听到，好像，当那家伙在脑海中闪过将要发生的事情时，停顿了一下;但是他知道他必须登录，而且他最好不要说他有，当他没有的时候，所以他说他没有。从那以后，谢尔库诺夫说，“你设定了你的最后期限;你可以改变它们。

一个教训足以让我的老板知道，为什么我不想做取代探索性研究的大工作，以及为什么我有理由不做吸收所有研究计算设施的速成工作。相反，我想使用这些工具来计算大量小问题。同样，在早期，我的计算能力有限，很明显，在我所在的地区，“数学家对机器没有用处”。但我需要更多的机器容量。每次我不得不告诉其他领域的科学家，“不，我不能;我没有机器容量，“他抱怨道。我说，''去告诉你的副总统，汉明需要更多的计算能力。过了一会儿，我可以看到顶部发生了什么;许多人对我的副总统说，''你的人需要更多的计算能力。知道了！

我还做了第二件事。当我借出我们在计算早期所拥有的一点编程能力时，我说，“我们的程序员没有得到他们应得的认可。当你发表一篇论文时，你会感谢那个程序员，否则你就不会再从我这里得到任何帮助。那位程序员将被点名感谢;她很努力。我等了几年。然后，我浏览了一年的BSTJ文章，并计算了感谢某个程序员的比例。我把它拿给老板说，'这就是计算在贝尔实验室发挥的核心作用;如果BSTJ很重要，那么计算就有多重要。他不得不屈服。你可以教育你的老板。这是一项艰巨的工作。在这次演讲中，我只是从下往上看;我不是从上到下看的。但我告诉你，尽管有高层管理人员，你怎么能得到你想要的东西。你也必须在那里推销你的想法。

好吧，我现在归结为这个话题，“成为一名伟大科学家的努力值得吗？要回答这个问题，你必须问人。当你超越他们的谦虚时，大多数人会说，“是的，做真正一流的工作，并且知道它，就像酒、女人和歌曲加在一起一样好，”或者如果是一个女人，她说，“这就像酒、男人和歌加在一起一样好。如果你看看老板们，他们往往会回来或要求报告，试图参与那些发现的时刻。他们总是挡路。所以很明显，那些已经做过的人，想再做一次。但这是一项有限的调查。我从来不敢出去问那些做得不好的人，他们对这件事有什么看法。这是一个有偏见的样本，但我仍然认为这是值得奋斗的。我认为，努力去做一流的工作绝对是值得的，因为事实是，斗争的价值大于结果。为自己做点什么而奋斗本身似乎是值得的。在我看来，成功和名声是一种红利。

我已经告诉过你怎么做。这很容易，那么为什么这么多人，尽管他们所有的才能，都失败了？例如，直到今天，我的观点是，在贝尔实验室的数学系里，有不少人比我更有能力，更有天赋，但他们的产量却没有那么多。他们中的一些人确实比我生产得更多;香农的产量比我多，其他一些人也生产了很多，但我的生产力很高，与许多其他装备更好的人相比。为什么会这样？他们怎么了？为什么那么多有前途的人都失败了？

嗯，原因之一是动力和承诺。那些能力较差但致力于此的人，比那些拥有高超技能并涉足它的人做得更多，他们白天工作，回家做其他事情，第二天回来工作。他们没有真正一流的工作显然需要的深刻承诺。他们做了很多好工作，但我们谈论的是一流的工作，记住。这是有区别的。好人，非常有才华的人，几乎总是能做出好工作。我们谈论的是杰出的工作，获得诺贝尔奖并得到认可的工作类型。

第二件事，我认为，是人格缺陷的问题。现在我要引用我在尔湾遇到的一个家伙。他曾是一个计算中心的负责人，他暂时被任命为大学校长的特别助理。很明显，他有一份前途光明的工作。有一次，他带我去他的办公室，向我展示了他写信的方法，以及他如何处理他的信件。他指出秘书的效率有多低。他把所有的信都堆在那里;他知道一切在哪里。他会用他的文字处理器把这封信拿出来。他吹嘘这是多么了不起，以及他如何在没有秘书干预的情况下完成如此多的工作。好吧，在他背后，我和秘书谈了谈。秘书说：“我当然帮不了他;我没有收到他的邮件。他不会给我登录的东西;我不知道他把它放在地板上的什么地方。我当然帮不了他。于是我去找他，说：'听着，如果你采用现在的方法，做你单枪匹马能做的事，你可以走那么远，不会比你单枪匹马能做的更远。如果你学会了与系统合作，你可以在系统支持你的情况下走得更远。而且，他再也没有走得更远。他有他的性格缺陷，想要完全控制，不愿意承认你需要系统的支持。

你发现这种情况一次又一次地发生;优秀的科学家会与系统作斗争，而不是学会与系统合作并利用系统所提供的一切。如果你学会如何使用它，它有很多。这需要耐心，但你可以学习如何很好地使用这个系统，你可以学习如何绕过它。毕竟，如果你想要一个“不”的决定，你只需要去找你的老板，然后很容易地得到一个“不”。如果你想做某事，不要问，去做。向他展示一个既成的事实。不要给他机会告诉你“不”。但是，如果你想要一个“不”，很容易得到一个“不”。

另一个人格缺陷是自我主张，在这种情况下，我将谈谈我自己的经历。我来自洛斯阿拉莫斯，早期我在纽约麦迪逊大道 590 号使用一台机器，我们只是在那里租用时间。我仍然穿着西式服装，大斜杠口袋，短裤和所有这些东西。我隐约注意到我没有得到像其他人那样好的服务。于是我开始测量。你进来了，你等着轮到你;我觉得我没有得到公平的交易。我对自己说，'为什么？IBM没有一个副总裁说过，“给汉明一个糟糕的时机”。是底层的秘书在做这件事。当一个插槽出现时，他们会急于找人溜进去，但他们出去找其他人。现在，为什么？我没有虐待他们。回答，我没有按照他们认为在这种情况下的人应该穿的衣服。归根结底就是——我穿得不合适。我必须做出决定——我是要坚持我的自我，按照我想要的方式穿衣服，让它不断地耗尽我职业生涯的努力，还是我要看起来更符合要求？我决定要努力让自己看起来符合要求。那一刻，我得到了更好的服务。而现在，作为一个老多彩的角色，我得到了比其他人更好的服务。

你应该根据听众的期望着装。如果我要在麻省理工学院计算机中心提供地址，我会穿上一件短袍和一件旧的灯芯绒夹克或其他东西。我知道，我不会让我的衣服、我的外表、我的举止妨碍我所关心的事情。许多科学家认为他们必须坚持自己的自我，并以自己的方式做事。他们必须能够做这个、那个或其他事情，并且他们付出稳定的价格。

约翰·图基（John Tukey）几乎总是穿着很随意。他会进入一个重要的办公室，过了很长时间，另一个人才意识到这是一个一流的人，他最好听。很长一段时间以来，约翰不得不克服这种敌意。这是白费力气！我没有说你应该顺从;我说：“顺从的外表会让你走得很远。如果你选择以任何方式维护你的自我，“我会按照我的方式去做”，那么你在整个职业生涯中都会付出一个小小的稳定代价。而这，在一生中，加起来就是大量不必要的麻烦。

通过不厌其烦地给秘书讲笑话，并且有点友好，我得到了极好的秘书帮助。例如，有一次，出于某种愚蠢的原因，Murray Hill的所有复制服务都被捆绑了。不要问我怎么做，但他们是。我想做点什么。我的秘书打电话给霍姆德尔的某个人，跳上公司的车，走了一个小时的路，把它复制了下来，然后回来了。这是对我努力让她振作起来、给她讲笑话和保持友好的回报;正是这点额外的工作后来为我带来了回报。通过意识到你必须使用这个系统并研究如何让系统完成你的工作，你就学会了如何使系统适应你的愿望。或者你可以一辈子稳定地战斗它，作为一场不宣而战的小战争。

我认为约翰·图基（John Tukey）付出了不必要的可怕代价。无论如何，他都是个天才，但我认为，如果他愿意顺从一点，而不是自我主张，那会更好，也更简单。他会一直按照自己想要的方式穿衣服。它不仅适用于着装，也适用于其他一千件事情;人们将继续与这个系统作斗争。并不是说你不应该偶尔！

当他们把图书馆从墨累山的中间搬到远端时，我的一个朋友提出了要自行车的要求。好吧，这个组织并不愚蠢。他们等了一会儿，发回了一张场地地图，上面写着：“请您在这张地图上标明您将要走的路线，以便我们获得涵盖您的保险单。又过了几个星期。然后他们问：“你打算把自行车存放在哪里，如何锁上，这样我们就可以这样做。他终于意识到，他当然会被红胶带绑死，所以他屈服了。他升任贝尔实验室总裁。

巴尼·奥利弗是个好人。他有一次给IEEE写了一封信。当时贝尔实验室的官方书架空间如此之大，IEEE论文集的高度也更大;由于你不能改变官方书架空间的大小，他给IEEE出版人写了一封信，说：“既然有这么多IEEE成员在贝尔实验室，而且官方空间如此之高，期刊的大小应该改变。他把它寄给老板签字。回来的是一张带有他签名的碳，但他仍然不知道原件是否寄出。我并不是说你不应该做出改革的姿态。我是说，我对有能力的人的研究是，他们不会让自己投入到那种战争中。他们玩了一会儿，然后放下它，继续他们的工作。

许多二流的家伙陷入了对系统的一些小问题，并将其带到了战争中。他把精力花在一个愚蠢的项目上。现在你要告诉我，必须有人改变这个系统。我同意;有人必须这样做。你想成为哪个？是改变系统的人还是做一流科学的人？你想成为哪个人？要清楚，当你与系统作斗争并与之斗争时，你在做什么，在多大程度上摆脱娱乐，以及与系统作斗争要浪费多少精力。我的建议是让别人来做，然后你就可以成为一名一流的科学家。你们中很少有人有能力既改革制度又成为一流的科学家。

另一方面，我们不能总是屈服。有些时候，一定程度的叛逆是明智的。据我观察，几乎所有的科学家都喜欢在一定程度上对这个系统进行调侃，因为纯粹是喜欢它。基本上可以归结为，如果不在其他领域具有独创性，您就无法在一个领域具有原创性。独创性是不同的。如果没有其他一些原创特征，你就不可能成为一个原创科学家。但是，许多科学家让他在其他地方的怪癖使他付出了比他或她获得的自我满足所必需的更高的代价。我不反对所有的自我主张;我反对一些人。

另一个错误是愤怒。科学家经常会生气，这是处理事情的方法。娱乐，是的，愤怒，不是。愤怒被误导了。你应该跟随和合作，而不是一直与系统作斗争。

您应该寻找的另一件事是事物的积极一面，而不是消极的一面。我已经举了几个例子，还有很多很多的例子;鉴于这种情况，我如何通过改变我看待它的方式，将明显的缺陷转化为资产。我再举一个例子。我是一个自负的人;这是毫无疑问的。我知道，大多数请假写书的人，都没有按时完成。所以在我离开之前，我告诉我所有的朋友，当我回来时，那本书就要完成了！是的，我会完成的——如果没有它，我会很惭愧地回来！我用我的自我让自己按照自己想要的方式行事。我吹嘘了一些东西，所以我必须表演。我发现很多次，就像一只走投无路的老鼠在真正的陷阱里，我的能力出奇地好。我发现说“哦，是的，我会在星期二给你答案”，却不知道该怎么做。到了星期天晚上，我真的很难想在周二之前我该如何交付。我经常把我的骄傲放在线上，有时我失败了，但正如我所说，就像一只走投无路的老鼠一样，我很惊讶我经常做得很好。我认为你需要学会使用自己。我认为你需要知道如何将情况从一种观点转换为另一种观点，这将增加成功的机会。

现在人类的自欺欺人非常非常普遍。有无数种方法可以改变一件事，开玩笑，让它看起来是另一种方式。当你问，“你为什么不做某某”时，这个人有一千个不在场证明。如果你看一下科学史，通常现在有 10 个人在那里准备好，我们为第一个在那里的人付出代价。其他九个人说，'嗯，我有这个想法，但我没有去做，等等。有这么多不在场证明。你为什么不是第一个？你为什么不做对？不要尝试不在场证明。不要试图自欺欺人。你可以告诉其他人你想要的所有不在场证明。我不介意。但对你自己来说，试着说实话。

如果你真的想成为一名一流的科学家，你需要了解你自己，了解你的弱点，你的长处，以及你的缺点，就像我的自负一样。如何将故障转换为资产？你怎么能改变你没有足够的人力进入一个方向的情况，而这正是你需要做的？我再说一遍，当我研究历史时，我看到成功的科学家改变了观点，缺陷变成了资产。

总而言之，我声称，这么多拥有伟大成就的人没有成功的一些原因是：他们不处理重要的问题，他们没有在情感上投入，他们没有尝试将困难的事情改变为其他容易做到但仍然重要的情况，他们不断给自己不在场证明为什么他们不这样做。他们一直说这是运气问题。我已经告诉过你这是多么容易;此外，我已经告诉过你如何改革。因此，勇往直前，成为伟大的科学家！

讨论 - 问题和答案

A. G. Chynoweth：嗯，那是 50 分钟的集中智慧和观察，在一个梦幻般的职业生涯中积累起来;我忘记了所有令人震惊的观察结果。其中一些非常非常及时。一个是请求增加计算机容量;今天早上，我一遍又一遍地从几个人那里听到这句话。所以今天这句话是正确的，尽管我们是在你发表类似言论的 20 到 30 年后，迪克。我能想到我们所有人都可以从你的演讲中吸取的各种教训。首先，当我将来在大厅里走来走去时，我希望我不会在 Bellcore 看到那么多紧闭的门。这是我认为非常有趣的一个观察结果。

非常感谢你，迪克;那是一个美妙的回忆。我现在将打开它以供提问。我相信有很多人想接受迪克提出的一些观点。

汉明：首先，让我回答一下 Alan Chynoweth 关于计算的问题。我在研究中从事计算机工作，10 年来，我一直告诉我的管理层，“把那台 ！&@#% 机器从研究中拿出来。我们一直被迫运行问题。我们无法进行研究，因为太忙于操作和运行计算机。最后，消息传了出去。他们打算将计算从研究中转移到其他地方。至少可以说，我是一个不受欢迎的人，我很惊讶人们没有踢我的小腿，因为每个人都被拿走了他们的玩具。我走进艾德·戴维的办公室，说，'听着，艾德，你必须给你的研究人员一台机器。如果你给他们一台巨大的机器，我们就会回到以前的麻烦中，忙于让它运转，我们无法思考。给他们最小的机器，因为他们是非常能干的人。他们将学习如何在小型机器上做事，而不是大规模计算。就我而言，UNIX 就是这样产生的。我们给了他们一台中等大小的机器，他们决定让它做伟大的事情。他们必须想出一个系统来做到这一点。它被称为 UNIX！

A. G. Chynoweth：我只需要拿起那个。迪克，在我们目前的环境中，当我们与监管机构或监管机构要求的一些繁文缛节作斗争时，有一句话是愤怒的 AVP 想出的，我一遍又一遍地使用它。他咆哮着说，“UNIX从来都不是可交付的！

问题：个人压力呢？这似乎有什么不同吗？

汉明：是的，确实如此。如果你没有情感上的参与，它就不会。我在贝尔实验室的大部分时间里都有早期溃疡。从那以后，我去了海军研究生院，稍微放松了一下，现在我的健康状况好多了。但如果你想成为一名伟大的科学家，你就必须忍受压力。你可以过上美好的生活;你可以是一个好人，也可以是一个伟大的科学家。但好人最后结束，是里奥·杜罗彻（Leo Durocher）说的。如果你想过上美好的幸福生活，有很多娱乐和其他一切，你就会过上美好的生活。

问题：关于有勇气的言论，没有人可以反驳;但是我们这些白发苍苍或地位高的人不必太担心。但是，我现在的年轻人感觉到，在竞争激烈的环境中，对冒险的真正担忧。你对此有什么智慧的话吗？

汉明：我会更多地引用 Ed David 的话。埃德·戴维（Ed David）担心我们社会中普遍失去神经。在我看来，我们确实经历了不同的时期。从战争中走出来，从我们制造原子弹的洛斯阿拉莫斯走出来，从建造雷达等等走出来，进入了数学系和研究领域，一群很有胆量的人。他们刚刚看到事情已经完成;他们刚刚赢得了一场精彩的战争。我们有理由鼓起勇气，因此我们做了很多事情。我不能安排这种情况再做一次。我不能责怪当代人没有它，但我同意你说的;我只是不能责怪它。在我看来，他们没有对伟大的渴望;他们缺乏这样做的勇气。但是我们有，因为我们处于有利的环境中拥有它;我们刚刚经历了一场非常成功的战争。在战争中，我们在很长一段时间内看起来非常非常糟糕;正如你所知道的，这是一场非常绝望的斗争。我认为，我们的成功给了我们勇气和自信;这就是为什么你看到，从四十年代末到五十年代，实验室的巨大生产力从早期就受到刺激。因为我们中的许多人以前被迫学习其他东西——我们被迫学习我们不想学习的东西，我们被迫敞开大门——然后我们可以利用我们学到的那些东西。这是真的，我对此无能为力;我也不能责怪当代人。这只是一个事实。

问题：管理层可以或应该做些什么吗？

汉明：管理层能做的很少。如果你想谈论管理研究，那是一个完全不同的谈话。我还要花一个小时。这个演讲是关于个人如何完成非常成功的研究，尽管管理层做了任何事情，或者尽管有任何其他反对意见。你是怎么做到的？就像我观察人们这样做一样。就是这么简单，就是这么难！

问题：头脑风暴是一个日常过程吗？

汉明：曾经这是一件非常受欢迎的事情，但似乎没有得到回报。就我自己而言，我觉得与其他人交谈是可取的;但是，头脑风暴很少是值得的。我确实会严格地与某人交谈，然后说，'看，我认为这里一定有什么东西。这是我想我看到的......”然后开始来回交谈。但你想挑选有能力的人。再打个比方，你知道这个概念叫做“临界质量”。如果你有足够的东西，你就有临界质量。还有一种我称之为“吸音器”的想法。当你得到太多的吸音器时，你会给出一个想法，而他们只是说，“是的，是的，是的。你要做的是让临界质量付诸行动;“是的，这让我想起了某某，”或者，“你有没有想过那个或这个？当你和其他人交谈时，你想摆脱那些好人，但只是说，“哦，是的”，并找到那些会刺激你的人。

例如，你不可能在不很快受到刺激的情况下与约翰·皮尔斯交谈。我曾经和一群人交谈过。例如，有埃德·吉尔伯特（Ed Gilbert）;我过去常常经常去他的办公室，问他问题，听他说话，回来后很兴奋。我小心翼翼地挑选了我的员工，我和谁一起做过，或者我没有集思广益，因为吸音器是一种诅咒。他们只是好人;它们填满了整个空间，除了吸收想法之外，它们什么也没贡献，新想法只是消失了，而不是回响。是的，我觉得有必要与人交谈。我认为闭门造车的人无法做到这一点，因此他们无法让自己的想法更加清晰，例如“你有没有注意到这边有什么东西？我从来不知道它——我可以过去看看。有人指路。在我访问这里时，我已经找到了几本书，我回家后必须阅读。当我认为人们可以回答我并给我我不知道的线索时，我会与人们交谈并提出问题。我出去看看！

问题：在分配阅读和写作时间以及实际进行研究时，您做了什么样的权衡？

汉明：在我早期的时候，我相信你应该花至少和你在原始研究上一样多的时间进行润色和演示。现在至少有 50% 的时间必须用于演示。这是一个很大的数字。

问题：图书馆工作应该付出多少努力？

汉明：这取决于领域。我会这样说。贝尔实验室有一个人，一个非常非常聪明的人。他总是在图书馆里;他阅读了一切。如果你想要参考资料，你就去找他，他给你各种各样的参考资料。但是在形成这些理论的过程中，我形成了一个命题：从长远来看，不会有以他的名字命名的效果。他现在从贝尔实验室退休，是一名兼职教授。他非常有价值;我不是在质疑这一点。他写了一些非常好的《物理评论》文章;但是没有以他的名字命名的效果，因为他读得太多了。如果你一直阅读别人的所作所为，你就会像他们一样思考。如果你想思考不同的想法，那就做很多有创造力的人所做的事情——把问题弄清楚，然后拒绝看任何答案，直到你仔细地思考问题，你会怎么做，你如何稍微改变问题，成为正确的问题。所以是的，你需要跟上。您需要跟上更多的步伐才能找出问题所在，而不是阅读以找到解决方案。阅读对于了解正在发生的事情以及可能的情况是必要的。但是，通过阅读来获得解决方案似乎并不是进行出色研究的方法。所以我给你两个答案。你读;但重要的不是数量，而是你阅读的方式。

问题：你如何让你的名字附在事物上？

汉明：通过做伟大的工作。我会告诉你汉明窗的。我给Tukey带来了很多次困难，我接到他从普林斯顿打给我的电话。我知道他在写功率谱，他问我是否介意他把某个窗口称为“汉明窗”。我对他说：'来吧，约翰;你很清楚，我只做了一小部分工作，但你也做了很多。他说：“是的，汉明，但你贡献了很多小事;你有权获得一些荣誉。所以他称它为汉明窗。现在，让我继续。我经常嘲笑约翰真正的伟大。我说过，真正的伟大是当你的名字像安培、瓦特和傅里叶一样时——当它用小写字母拼写时。汉明窗就是这样来的。

问题：迪克，你愿意评论一下演讲、写论文和写书之间的相对有效性吗？

汉明：在短期内，如果你想明天刺激某人，论文非常重要。如果你想长期获得认可，在我看来，写书更多的是贡献，因为我们大多数人都需要定位。在这个知识几乎无限的时代，我们需要方向来找到自己的道路。让我告诉你什么是无限的知识。从牛顿时代到现在，我们的知识几乎每 17 年翻一番，或多或少。我们基本上通过专业化来应对这个问题。按照这个速度，在未来的340年里，将有20个翻倍，即100万个，现在每个领域将有100万个专业领域。这不会发生。目前知识的增长将自我扼杀，直到我们获得不同的工具。我相信，那些试图消化、协调、摆脱重复、摆脱不那么富有成效的方法并清楚地呈现我们现在所知道的基本思想的书籍，将是后代将珍视的东西。公开演讲是必要的;私下会谈是必要的;书面论文是必要的。但我倾向于相信，从长远来看，省略不重要的东西的书比告诉你一切的书更重要，因为你不想知道一切。我不想知道那么多关于企鹅的事情是通常的回答。你只想知道本质。

问题：你提到了诺贝尔奖的问题，以及随后对一些职业的恶名。这难道不是一个更宽泛的名声问题吗？一个人能做什么？

汉明：您可以做的一些事情如下。大约每七年，在你的领域做出一次重大的（如果不是完全的）转变。因此，我定期从数值分析转向硬件，再到软件等等，因为你往往会用尽你的想法。当你进入一个新的领域时，你必须像婴儿一样重新开始。你不再是大麂麝香，你可以从那里开始，你可以开始种植那些橡子，这些橡子将成为巨大的橡树。我相信，香农毁了自己。事实上，当他离开贝尔实验室时，我说，“香农的科学生涯就这样结束了。我从朋友那里收到了很多抨击，他们说香农一如既往地聪明。我说，'是的，他会同样聪明，但这就是他科学生涯的终结，'我真的相信是这样。

你必须改变。过了一会儿你就会累;你在一个领域用尽了你的独创性。你需要在附近买点东西。我并不是说你从音乐转向理论物理学再到英国文学;我的意思是，在你的领域内，你应该改变区域，这样你就不会过时。你不能强迫每七年改变一次，但如果可以的话，我会要求你做一个研究的条件，就是你每七年改变一次你的研究领域，并合理地定义它意味着什么，或者在10年结束时，管理层有权强迫你改变。我会坚持改变，因为我是认真的。老家伙们发生的事情是，他们掌握了一种技术;他们继续使用它。他们正朝着那个方向前进，当时是正确的，但世界变了。有新的方向;但老家伙们仍然朝着他们以前的方向前进。

你需要进入一个新的领域来获得新的观点，并且在你用完所有旧观点之前。你可以为此做点什么，但这需要努力和精力。说：“是的，我会放弃我的名声，这需要勇气。例如，当纠错码被很好地推出时，有了这些理论，我说，“汉明，你要停止阅读该领域的论文了;你将完全忽略它;你要试着做点别的事情，而不是在那上面滑行。我故意拒绝继续从事这个领域。我甚至不会看报纸来强迫自己有机会做别的事情。我管理了自己，这就是我在整个演讲中所宣讲的。我知道我自己的许多缺点，所以我管理自己。我有很多缺点，所以我有很多问题，即管理的可能性很多。

问题：你会比较研究和管理吗？

汉明：如果你想成为一名伟大的研究人员，你不会成为公司的总裁。如果你想成为公司的总裁，那是另一回事。我不反对担任公司总裁。我只是不想。我认为伊恩·罗斯（Ian Ross）作为贝尔实验室的总裁做得很好。我不反对;但你必须清楚你想要什么。此外，当你年轻的时候，你可能已经选择了成为一名伟大的科学家，但随着你寿命的延长，你可能会改变主意。例如，有一天我去找我的老板博德，问他：“你为什么会成为部门主管？你为什么不做一个好科学家呢？他说，“汉明，我对贝尔实验室的数学应该是什么样子有一个愿景。我看到如果这个愿景要实现，我必须实现它;我必须成为部门主管。当你对自己想做的事情的愿景是你可以单枪匹马做的事情时，那么你应该追求它。有一天，你的愿景，你认为需要做的事情，比你单枪匹马所能做的事情更大，那么你就必须转向管理。愿景越大，你必须在管理上走得越远。如果你对整个实验室或整个贝尔系统应该是什么样子有一个愿景，你必须到达那里才能实现它。你不能很容易地从底部实现它。这取决于你有什么目标和愿望。当他们在生活中发生变化时，你必须准备好改变。我选择避免管理，因为我更喜欢单枪匹马地做我能做的事情。但这是我做出的选择，而且是有偏见的。每个人都有权选择。保持开放的心态。但是，当你选择一条道路时，看在天堂的份上，要意识到你做了什么，你做了什么，你做出了选择。不要试图两面都做。

问题：一个人的期望有多重要，或者在一个团队中或周围被期望你做出出色工作的人有多重要？

汉明：在贝尔实验室，每个人都希望我能做出好的工作——这对我有很大的帮助。每个人都希望你做得很好，所以如果你有自豪感，你就去做。我认为身边有一流的人是非常有价值的。我寻找最优秀的人。物理桌失去最优秀的人的那一刻，我离开了。当我看到化学表也是如此的那一刻，我就离开了。我试着和那些能力很强的人一起去，这样我就可以向他们学习，并期望我能取得好成绩。通过刻意管理自己，我认为我比自由放任做得更好。

问题：在演讲开始时，你最小化或淡化了运气;但你似乎也掩盖了把你带到洛斯阿拉莫斯，把你带到芝加哥，把你带到贝尔实验室的情况。

汉明：有一些运气。另一方面，我不知道备用分支。除非你能说其他分支不会同样或更成功，否则我不能说。你做的特别的事情是运气吗？例如，当我在洛斯阿拉莫斯见到费曼时，我知道他将获得诺贝尔奖。我不知道为什么。但我很清楚他会做伟大的工作。无论将来出现什么方向，这个人都会做伟大的工作。果然，他确实做得很好。并不是说你在这种情况下只做了一点点伟大的工作，那是运气，迟早有很多机会。有一大堆机会，如果你处于这种情况，你就会抓住一个机会，你在那边而不是在这里很棒。有运气的成分，是和否。运气眷顾有准备的头脑;运气眷顾有准备的人。不能保证;我不保证成功是绝对确定的。我会说运气会改变赔率，但个人有一些明确的控制。

那么，去吧，做伟大的工作！

You and Your Research, by Richard Hamming

Richard Hamming gave this talk in March of 1986. [1]  It's one of the best talks I've ever read and has long impacted how I think about spending my time.

I mentioned it to a number of people this weekend who, to my surprise, had never heard of it.  So I though I'd share it here:

[Addition 5/28/23: see this great annotated version from Gwern.]

It's a pleasure to be here. I doubt if I can live up to the Introduction. The title of my talk is, ``You and Your Research.'' It is not about managing research, it is about how you individually do your research. I could give a talk on the other subject - but it's not, it's about you. I'm not talking about ordinary run-of-the-mill research; I'm talking about great research. And for the sake of describing great research I'll occasionally say Nobel-Prize type of work. It doesn't have to gain the Nobel Prize, but I mean those kinds of things which we perceive are significant things. Relativity, if you want, Shannon's information theory, any number of outstanding theories - that's the kind of thing I'm talking about.

Now, how did I come to do this study? At Los Alamos I was brought in to run the computing machines which other people had got going, so those scientists and physicists could get back to business. I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious. I wanted to know why they were so different from me. I saw Feynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw Hans Bethe: he was my boss. I saw quite a few very capable people. I became very interested in the difference between those who do and those who might have done.

When I came to Bell Labs, I came into a very productive department. Bode was the department head at the time; Shannon was there, and there were other people. I continued examining the questions, ``Why?'' and ``What is the difference?'' I continued subsequently by reading biographies, autobiographies, asking people questions such as: ``How did you come to do this?'' I tried to find out what are the differences. And that's what this talk is about.

Now, why is this talk important? I think it is important because, as far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn't do you any good from one life to the next! Why shouldn't you do significant things in this one life, however you define significant? I'm not going to define it - you know what I mean. I will talk mainly about science because that is what I have studied. But so far as I know, and I've been told by others, much of what I say applies to many fields. Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.

In order to get at you individually, I must talk in the first person. I have to get you to drop modesty and say to yourself, ``Yes, I would like to do first-class work.'' Our society frowns on people who set out to do really good work. You're not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that's a kind of dumb thing to say. I say, why shouldn't you set out to do something significant. You don't have to tell other people, but shouldn't you say to yourself, ``Yes, I would like to do something significant.''

In order to get to the second stage, I have to drop modesty and talk in the first person about what I've seen, what I've done, and what I've heard. I'm going to talk about people, some of whom you know, and I trust that when we leave, you won't quote me as saying some of the things I said.

Let me start not logically, but psychologically. I find that the major objection is that people think great science is done by luck. It's all a matter of luck. Well, consider Einstein. Note how many different things he did that were good. Was it all luck? Wasn't it a little too repetitive? Consider Shannon. He didn't do just information theory. Several years before, he did some other good things and some which are still locked up in the security of cryptography. He did many good things.

You see again and again, that it is more than one thing from a good person. Once in a while a person does only one thing in his whole life, and we'll talk about that later, but a lot of times there is repetition. I claim that luck will not cover everything. And I will cite Pasteur who said, ``Luck favors the prepared mind.'' And I think that says it the way I believe it. There is indeed an element of luck, and no, there isn't. The prepared mind sooner or later finds something important and does it. So yes, it is luck. The particular thing you do is luck, but that you do something is not.

For example, when I came to Bell Labs, I shared an office for a while with Shannon. At the same time he was doing information theory, I was doing coding theory. It is suspicious that the two of us did it at the same place and at the same time - it was in the atmosphere. And you can say, ``Yes, it was luck.'' On the other hand you can say, ``But why of all the people in Bell Labs then were those the two who did it?'' Yes, it is partly luck, and partly it is the prepared mind; but `partly' is the other thing I'm going to talk about. So, although I'll come back several more times to luck, I want to dispose of this matter of luck as being the sole criterion whether you do great work or not. I claim you have some, but not total, control over it. And I will quote, finally, Newton on the matter. Newton said, ``If others would think as hard as I did, then they would get similar results.''

One of the characteristics you see, and many people have it including great scientists, is that usually when they were young they had independent thoughts and had the courage to pursue them. For example, Einstein, somewhere around 12 or 14, asked himself the question, ``What would a light wave look like if I went with the velocity of light to look at it?'' Now he knew that electromagnetic theory says you cannot have a stationary local maximum. But if he moved along with the velocity of light, he would see a local maximum. He could see a contradiction at the age of 12, 14, or somewhere around there, that everything was not right and that the velocity of light had something peculiar. Is it luck that he finally created special relativity? Early on, he had laid down some of the pieces by thinking of the fragments. Now that's the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.

How about having lots of `brains?' It sounds good. Most of you in this room probably have more than enough brains to do first-class work. But great work is something else than mere brains. Brains are measured in various ways. In mathematics, theoretical physics, astrophysics, typically brains correlates to a great extent with the ability to manipulate symbols. And so the typical IQ test is apt to score them fairly high. On the other hand, in other fields it is something different. For example, Bill Pfann, the fellow who did zone melting, came into my office one day. He had this idea dimly in his mind about what he wanted and he had some equations. It was pretty clear to me that this man didn't know much mathematics and he wasn't really articulate. His problem seemed interesting so I took it home and did a little work. I finally showed him how to run computers so he could compute his own answers. I gave him the power to compute. He went ahead, with negligible recognition from his own department, but ultimately he has collected all the prizes in the field. Once he got well started, his shyness, his awkwardness, his inarticulateness, fell away and he became much more productive in many other ways. Certainly he became much more articulate.

And I can cite another person in the same way. I trust he isn't in the audience, i.e. a fellow named Clogston. I met him when I was working on a problem with John Pierce's group and I didn't think he had much. I asked my friends who had been with him at school, ``Was he like that in graduate school?'' ``Yes,'' they replied. Well I would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.

One of the characteristics of successful scientists is having courage. Once you get your courage up and believe that you can do important problems, then you can. If you think you can't, almost surely you are not going to. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He wants to create a method of coding, but he doesn't know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, ``What would the average random code do?'' He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.

Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. It is not that they don't do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late. I don't know how whatever field you are in fits this scale, but age has some effect.

But let me say why age seems to have the effect it does. In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, Brattain, practically with tears in his eyes, said, ``I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.'' Well I said to myself, ``That is nice.'' But in a few weeks I saw it was affecting him. Now he could only work on great problems.

When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren't good afterwards, but they were superb before they got there and were only good afterwards.

This brings up the subject, out of order perhaps, of working conditions. What most people think are the best working conditions, are not. Very clearly they are not because people are often most productive when working conditions are bad. One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.

I give you a story from my own private life. Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren't going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, ``Did I want to go or not?'' and I wondered how I could get the best of two possible worlds. I finally said to myself, ``Hamming, you think the machines can do practically everything. Why can't you make them write programs?'' What appeared at first to me as a defect forced me into automatic programming very early. What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, ``Gee, I'm never going to get enough programmers, so how can I ever do any great programming?''

And there are many other stories of the same kind; Grace Hopper has similar ones. I think that if you look carefully you will see that often the great scientists, by turning the problem around a bit, changed a defect to an asset. For example, many scientists when they found they couldn't do a problem finally began to study why not. They then turned it around the other way and said, ``But of course, this is what it is'' and got an important result. So ideal working conditions are very strange. The ones you want aren't always the best ones for you.

Now for the matter of drive. You observe that most great scientists have tremendous drive. I worked for ten years with John Tukey at Bell Labs. He had tremendous drive. One day about three or four years after I joined, I discovered that John Tukey was slightly younger than I was. John was a genius and I clearly was not. Well I went storming into Bode's office and said, ``How can anybody my age know as much as John Tukey does?'' He leaned back in his chair, put his hands behind his head, grinned slightly, and said, ``You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.'' I simply slunk out of the office!

What Bode was saying was this: ``Knowledge and productivity are like compound interest.'' Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity - it is very much like compound interest. I don't want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime. I took Bode's remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and I found, in fact, I could get more work done. I don't like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There's no question about this.

On this matter of drive Edison says, ``Genius is 99% perspiration and 1% inspiration.'' He may have been exaggerating, but the idea is that solid work, steadily applied, gets you surprisingly far. The steady application of effort with a little bit more work, intelligently applied is what does it. That's the trouble; drive, misapplied, doesn't get you anywhere. I've often wondered why so many of my good friends at Bell Labs who worked as hard or harder than I did, didn't have so much to show for it. The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.

There's another trait on the side which I want to talk about; that trait is ambiguity. It took me a while to discover its importance. Most people like to believe something is or is not true. Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you'll never notice the flaws; if you doubt too much you won't get started. It requires a lovely balance. But most great scientists are well aware of why their theories are true and they are also well aware of some slight misfits which don't quite fit and they don't forget it. Darwin writes in his autobiography that he found it necessary to write down every piece of evidence which appeared to contradict his beliefs because otherwise they would disappear from his mind. When you find apparent flaws you've got to be sensitive and keep track of those things, and keep an eye out for how they can be explained or how the theory can be changed to fit them. Those are often the great contributions. Great contributions are rarely done by adding another decimal place. It comes down to an emotional commitment. Most great scientists are completely committed to their problem. Those who don't become committed seldom produce outstanding, first-class work.

Now again, emotional commitment is not enough. It is a necessary condition apparently. And I think I can tell you the reason why. Everybody who has studied creativity is driven finally to saying, ``creativity comes out of your subconscious.'' Somehow, suddenly, there it is. It just appears. Well, we know very little about the subconscious; but one thing you are pretty well aware of is that your dreams also come out of your subconscious. And you're aware your dreams are, to a fair extent, a reworking of the experiences of the day. If you are deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem. And so you wake up one morning, or on some afternoon, and there's the answer. For those who don't get committed to their current problem, the subconscious goofs off on other things and doesn't produce the big result. So the way to manage yourself is that when you have a real important problem you don't let anything else get the center of your attention - you keep your thoughts on the problem. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.

Now Alan Chynoweth mentioned that I used to eat at the physics table. I had been eating with the mathematicians and I found out that I already knew a fair amount of mathematics; in fact, I wasn't learning much. The physics table was, as he said, an exciting place, but I think he exaggerated on how much I contributed. It was very interesting to listen to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other people, and I was learning a lot. But unfortunately a Nobel Prize came, and a promotion came, and what was left was the dregs. Nobody wanted what was left. Well, there was no use eating with them!

Over on the other side of the dining hall was a chemistry table. I had worked with one of the fellows, Dave McCall; furthermore he was courting our secretary at the time. I went over and said, ``Do you mind if I join you?'' They can't say no, so I started eating with them for a while. And I started asking, ``What are the important problems of your field?'' And after a week or so, ``What important problems are you working on?'' And after some more time I came in one day and said, ``If what you are doing is not important, and if you don't think it is going to lead to something important, why are you at Bell Labs working on it?'' I wasn't welcomed after that; I had to find somebody else to eat with! That was in the spring.

In the fall, Dave McCall stopped me in the hall and said, ``Hamming, that remark of yours got underneath my skin. I thought about it all summer, i.e. what were the important problems in my field. I haven't changed my research,'' he says, ``but I think it was well worthwhile.'' And I said, ``Thank you Dave,'' and went on. I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles. They were unable to ask themselves, ``What are the important problems in my field?''

If you do not work on an important problem, it's unlikely you'll do important work. It's perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, `important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don't work on important problems, I mean it in that sense. The average scientist, so far as I can make out, spends almost all his time working on problems which he believes will not be important and he also doesn't believe that they will lead to important problems.

I spoke earlier about planting acorns so that oaks will grow. You can't always know exactly where to be, but you can keep active in places where something might happen. And even if you believe that great science is a matter of luck, you can stand on a mountain top where lightning strikes; you don't have to hide in the valley where you're safe. But the average scientist does routine safe work almost all the time and so he (or she) doesn't produce much. It's that simple. If you want to do great work, you clearly must work on important problems, and you should have an idea.

Along those lines at some urging from John Tukey and others, I finally adopted what I called ``Great Thoughts Time.'' When I went to lunch Friday noon, I would only discuss great thoughts after that. By great thoughts I mean ones like: ``What will be the role of computers in all of AT&T?'', ``How will computers change science?'' For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. nine out of ten experiments would be done on the computer and one in ten in the lab. They knew I was a crazy mathematician and had no sense of reality. I knew they were wrong and they've been proved wrong while I have been proved right. They built laboratories when they didn't need them. I saw that computers were transforming science because I spent a lot of time asking ``What will be the impact of computers on science and how can I change it?'' I asked myself, ``How is it going to change Bell Labs?'' I remarked one time, in the same address, that more than one-half of the people at Bell Labs will be interacting closely with computing machines before I leave. Well, you all have terminals now. I thought hard about where was my field going, where were the opportunities, and what were the important things to do. Let me go there so there is a chance I can do important things.

Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, one hears them say ``Well that bears on this problem.'' They drop all the other things and get after it. Now I can tell you a horror story that was told to me but I can't vouch for the truth of it. I was sitting in an airport talking to a friend of mine from Los Alamos about how it was lucky that the fission experiment occurred over in Europe when it did because that got us working on the atomic bomb here in the US. He said ``No; at Berkeley we had gathered a bunch of data; we didn't get around to reducing it because we were building some more equipment, but if we had reduced that data we would have found fission.'' They had it in their hands and they didn't pursue it. They came in second!

The great scientists, when an opportunity opens up, get after it and they pursue it. They drop all other things. They get rid of other things and they get after an idea because they had already thought the thing through. Their minds are prepared; they see the opportunity and they go after it. Now of course lots of times it doesn't work out, but you don't have to hit many of them to do some great science. It's kind of easy. One of the chief tricks is to live a long time!

Another trait, it took me a while to notice. I noticed the following facts about people who work with the door open or the door closed. I notice that if you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don't know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, ``The closed door is symbolic of a closed mind.'' I don't know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing - not much, but enough that they miss fame.

I want to talk on another topic. It is based on the song which I think many of you know, ``It ain't what you do, it's the way that you do it.'' I'll start with an example of my own. I was conned into doing on a digital computer, in the absolute binary days, a problem which the best analog computers couldn't do. And I was getting an answer. When I thought carefully and said to myself, ``You know, Hamming, you're going to have to file a report on this military job; after you spend a lot of money you're going to have to account for it and every analog installation is going to want the report to see if they can't find flaws in it.'' I was doing the required integration by a rather crummy method, to say the least, but I was getting the answer. And I realized that in truth the problem was not just to get the answer; it was to demonstrate for the first time, and beyond question, that I could beat the analog computer on its own ground with a digital machine. I reworked the method of solution, created a theory which was nice and elegant, and changed the way we computed the answer; the results were no different. The published report had an elegant method which was later known for years as ``Hamming's Method of Integrating Differential Equations.'' It is somewhat obsolete now, but for a while it was a very good method. By changing the problem slightly, I did important work rather than trivial work.

In the same way, when using the machine up in the attic in the early days, I was solving one problem after another after another; a fair number were successful and there were a few failures. I went home one Friday after finishing a problem, and curiously enough I wasn't happy; I was depressed. I could see life being a long sequence of one problem after another after another. After quite a while of thinking I decided, ``No, I should be in the mass production of a variable product. I should be concerned with all of next year's problems, not just the one in front of my face.'' By changing the question I still got the same kind of results or better, but I changed things and did important work. I attacked the major problem - How do I conquer machines and do all of next year's problems when I don't know what they are going to be? How do I prepare for it? How do I do this one so I'll be on top of it? How do I obey Newton's rule? He said, ``If I have seen further than others, it is because I've stood on the shoulders of giants.'' These days we stand on each other's feet!

You should do your job in such a fashion that others can build on top of it, so they will indeed say, ``Yes, I've stood on so and so's shoulders and I saw further.'' The essence of science is cumulative. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

Now if you are much of a mathematician you know that the effort to generalize often means that the solution is simple. Often by stopping and saying, ``This is the problem he wants but this is characteristic of so and so. Yes, I can attack the whole class with a far superior method than the particular one because I was earlier embedded in needless detail.'' The business of abstraction frequently makes things simple. Furthermore, I filed away the methods and prepared for the future problems.

To end this part, I'll remind you, ``It is a poor workman who blames his tools - the good man gets on with the job, given what he's got, and gets the best answer he can.'' And I suggest that by altering the problem, by looking at the thing differently, you can make a great deal of difference in your final productivity because you can either do it in such a fashion that people can indeed build on what you've done, or you can do it in such a fashion that the next person has to essentially duplicate again what you've done. It isn't just a matter of the job, it's the way you write the report, the way you write the paper, the whole attitude. It's just as easy to do a broad, general job as one very special case. And it's much more satisfying and rewarding!

I have now come down to a topic which is very distasteful; it is not sufficient to do a job, you have to sell it. `Selling' to a scientist is an awkward thing to do. It's very ugly; you shouldn't have to do it. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you've done, read it, and come back and say, ``Yes, that was good.'' I suggest that when you open a journal, as you turn the pages, you ask why you read some articles and not others. You had better write your report so when it is published in the Physical Review, or wherever else you want it, as the readers are turning the pages they won't just turn your pages but they will stop and read yours. If they don't stop and read it, you won't get credit.

There are three things you have to do in selling. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. We had a lot of so-called `back room scientists.' In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. They would not stand up right in the middle of a hot conference, in the middle of activity, and say, ``We should do this for these reasons.'' You need to master that form of communication as well as prepared speeches.

When I first started, I got practically physically ill while giving a speech, and I was very, very nervous. I realized I either had to learn to give speeches smoothly or I would essentially partially cripple my whole career. The first time IBM asked me to give a speech in New York one evening, I decided I was going to give a really good speech, a speech that was wanted, not a technical one but a broad one, and at the end if they liked it, I'd quietly say, ``Any time you want one I'll come in and give you one.'' As a result, I got a great deal of practice giving speeches to a limited audience and I got over being afraid. Furthermore, I could also then study what methods were effective and what were ineffective.

While going to meetings I had already been studying why some papers are remembered and most are not. The technical person wants to give a highly limited technical talk. Most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. As a result, many talks are ineffective. The speaker names a topic and suddenly plunges into the details he's solved. Few people in the audience may follow. You should paint a general picture to say why it's important, and then slowly give a sketch of what was done. Then a larger number of people will say, ``Yes, Joe has done that,'' or ``Mary has done that; I really see where it is; yes, Mary really gave a good talk; I understand what Mary has done.'' The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information. So I say this idea of selling is obvious.

Let me summarize. You've got to work on important problems. I deny that it is all luck, but I admit there is a fair element of luck. I subscribe to Pasteur's ``Luck favors the prepared mind.'' I favor heavily what I did. Friday afternoons for years - great thoughts only - means that I committed 10% of my time trying to understand the bigger problems in the field, i.e. what was and what was not important. I found in the early days I had believed `this' and yet had spent all week marching in `that' direction. It was kind of foolish. If I really believe the action is over there, why do I march in this direction? I either had to change my goal or change what I did. So I changed something I did and I marched in the direction I thought was important. It's that easy.

Now you might tell me you haven't got control over what you have to work on. Well, when you first begin, you may not. But once you're moderately successful, there are more people asking for results than you can deliver and you have some power of choice, but not completely. I'll tell you a story about that, and it bears on the subject of educating your boss. I had a boss named Schelkunoff; he was, and still is, a very good friend of mine. Some military person came to me and demanded some answers by Friday. Well, I had already dedicated my computing resources to reducing data on the fly for a group of scientists; I was knee deep in short, small, important problems. This military person wanted me to solve his problem by the end of the day on Friday. I said, ``No, I'll give it to you Monday. I can work on it over the weekend. I'm not going to do it now.'' He goes down to my boss, Schelkunoff, and Schelkunoff says, ``You must run this for him; he's got to have it by Friday.'' I tell him, ``Why do I?''; he says, ``You have to.'' I said, ``Fine, Sergei, but you're sitting in your office Friday afternoon catching the late bus home to watch as this fellow walks out that door.'' I gave the military person the answers late Friday afternoon. I then went to Schelkunoff's office and sat down; as the man goes out I say, ``You see Schelkunoff, this fellow has nothing under his arm; but I gave him the answers.'' On Monday morning Schelkunoff called him up and said, ``Did you come in to work over the weekend?'' I could hear, as it were, a pause as the fellow ran through his mind of what was going to happen; but he knew he would have had to sign in, and he'd better not say he had when he hadn't, so he said he hadn't. Ever after that Schelkunoff said, ``You set your deadlines; you can change them.''

One lesson was sufficient to educate my boss as to why I didn't want to do big jobs that displaced exploratory research and why I was justified in not doing crash jobs which absorb all the research computing facilities. I wanted instead to use the facilities to compute a large number of small problems. Again, in the early days, I was limited in computing capacity and it was clear, in my area, that a ``mathematician had no use for machines.'' But I needed more machine capacity. Every time I had to tell some scientist in some other area, ``No I can't; I haven't the machine capacity,'' he complained. I said ``Go tell your Vice President that Hamming needs more computing capacity.'' After a while I could see what was happening up there at the top; many people said to my Vice President, ``Your man needs more computing capacity.'' I got it!

I also did a second thing. When I loaned what little programming power we had to help in the early days of computing, I said, ``We are not getting the recognition for our programmers that they deserve. When you publish a paper you will thank that programmer or you aren't getting any more help from me. That programmer is going to be thanked by name; she's worked hard.'' I waited a couple of years. I then went through a year of BSTJ articles and counted what fraction thanked some programmer. I took it into the boss and said, ``That's the central role computing is playing in Bell Labs; if the BSTJ is important, that's how important computing is.'' He had to give in. You can educate your bosses. It's a hard job. In this talk I'm only viewing from the bottom up; I'm not viewing from the top down. But I am telling you how you can get what you want in spite of top management. You have to sell your ideas there also.

Well I now come down to the topic, ``Is the effort to be a great scientist worth it?'' To answer this, you must ask people. When you get beyond their modesty, most people will say, ``Yes, doing really first-class work, and knowing it, is as good as wine, women and song put together,'' or if it's a woman she says, ``It is as good as wine, men and song put together.'' And if you look at the bosses, they tend to come back or ask for reports, trying to participate in those moments of discovery. They're always in the way. So evidently those who have done it, want to do it again. But it is a limited survey. I have never dared to go out and ask those who didn't do great work how they felt about the matter. It's a biased sample, but I still think it is worth the struggle. I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.

I've told you how to do it. It is so easy, so why do so many people, with all their talents, fail? For example, my opinion, to this day, is that there are in the mathematics department at Bell Labs quite a few people far more able and far better endowed than I, but they didn't produce as much. Some of them did produce more than I did; Shannon produced more than I did, and some others produced a lot, but I was highly productive against a lot of other fellows who were better equipped. Why is it so? What happened to them? Why do so many of the people who have great promise, fail?

Well, one of the reasons is drive and commitment. The people who do great work with less ability but who are committed to it, get more done that those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don't have the deep commitment that is apparently necessary for really first-class work. They turn out lots of good work, but we were talking, remember, about first-class work. There is a difference. Good people, very talented people, almost always turn out good work. We're talking about the outstanding work, the type of work that gets the Nobel Prize and gets recognition.

The second thing is, I think, the problem of personality defects. Now I'll cite a fellow whom I met out in Irvine. He had been the head of a computing center and he was temporarily on assignment as a special assistant to the president of the university. It was obvious he had a job with a great future. He took me into his office one time and showed me his method of getting letters done and how he took care of his correspondence. He pointed out how inefficient the secretary was. He kept all his letters stacked around there; he knew where everything was. And he would, on his word processor, get the letter out. He was bragging how marvelous it was and how he could get so much more work done without the secretary's interference. Well, behind his back, I talked to the secretary. The secretary said, ``Of course I can't help him; I don't get his mail. He won't give me the stuff to log in; I don't know where he puts it on the floor. Of course I can't help him.'' So I went to him and said, ``Look, if you adopt the present method and do what you can do single-handedly, you can go just that far and no farther than you can do single-handedly. If you will learn to work with the system, you can go as far as the system will support you.'' And, he never went any further. He had his personality defect of wanting total control and was not willing to recognize that you need the support of the system.

You find this happening again and again; good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer. It has a lot, if you learn how to use it. It takes patience, but you can learn how to use the system pretty well, and you can learn how to get around it. After all, if you want a decision `No', you just go to your boss and get a `No' easy. If you want to do something, don't ask, do it. Present him with an accomplished fact. Don't give him a chance to tell you `No'. But if you want a `No', it's easy to get a `No'.

Another personality defect is ego assertion and I'll speak in this case of my own experience. I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, ``Why? No Vice President at IBM said, `Give Hamming a bad time'. It is the secretaries at the bottom who are doing this. When a slot appears, they'll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven't mistreated them.'' Answer, I wasn't dressing the way they felt somebody in that situation should. It came down to just that - I wasn't dressing properly. I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people.

You should dress according to the expectations of the audience spoken to. If I am going to give an address at the MIT computer center, I dress with a bolo and an old corduroy jacket or something else. I know enough not to let my clothes, my appearance, my manners get in the way of what I care about. An enormous number of scientists feel they must assert their ego and do their thing their way. They have got to be able to do this, that, or the other thing, and they pay a steady price.

John Tukey almost always dressed very casually. He would go into an important office and it would take a long time before the other fellow realized that this is a first-class man and he had better listen. For a long time John has had to overcome this kind of hostility. It's wasted effort! I didn't say you should conform; I said ``The appearance of conforming gets you a long way.'' If you chose to assert your ego in any number of ways, ``I am going to do it my way,'' you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble.

By taking the trouble to tell jokes to the secretaries and being a little friendly, I got superb secretarial help. For instance, one time for some idiot reason all the reproducing services at Murray Hill were tied up. Don't ask me how, but they were. I wanted something done. My secretary called up somebody at Holmdel, hopped the company car, made the hour-long trip down and got it reproduced, and then came back. It was a payoff for the times I had made an effort to cheer her up, tell her jokes and be friendly; it was that little extra work that later paid off for me. By realizing you have to use the system and studying how to get the system to do your work, you learn how to adapt the system to your desires. Or you can fight it steadily, as a small undeclared war, for the whole of your life.

And I think John Tukey paid a terrible price needlessly. He was a genius anyhow, but I think it would have been far better, and far simpler, had he been willing to conform a little bit instead of ego asserting. He is going to dress the way he wants all of the time. It applies not only to dress but to a thousand other things; people will continue to fight the system. Not that you shouldn't occasionally!

When they moved the library from the middle of Murray Hill to the far end, a friend of mine put in a request for a bicycle. Well, the organization was not dumb. They waited awhile and sent back a map of the grounds saying, ``Will you please indicate on this map what paths you are going to take so we can get an insurance policy covering you.'' A few more weeks went by. They then asked, ``Where are you going to store the bicycle and how will it be locked so we can do so and so.'' He finally realized that of course he was going to be red-taped to death so he gave in. He rose to be the President of Bell Laboratories.

Barney Oliver was a good man. He wrote a letter one time to the IEEE. At that time the official shelf space at Bell Labs was so much and the height of the IEEE Proceedings at that time was larger; and since you couldn't change the size of the official shelf space he wrote this letter to the IEEE Publication person saying, ``Since so many IEEE members were at Bell Labs and since the official space was so high the journal size should be changed.'' He sent it for his boss's signature. Back came a carbon with his signature, but he still doesn't know whether the original was sent or not. I am not saying you shouldn't make gestures of reform. I am saying that my study of able people is that they don't get themselves committed to that kind of warfare. They play it a little bit and drop it and get on with their work.

Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Now you are going to tell me that somebody has to change the system. I agree; somebody's has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist.

On the other hand, we can't always give in. There are times when a certain amount of rebellion is sensible. I have observed almost all scientists enjoy a certain amount of twitting the system for the sheer love of it. What it comes down to basically is that you cannot be original in one area without having originality in others. Originality is being different. You can't be an original scientist without having some other original characteristics. But many a scientist has let his quirks in other places make him pay a far higher price than is necessary for the ego satisfaction he or she gets. I'm not against all ego assertion; I'm against some.

Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time.

Another thing you should look for is the positive side of things instead of the negative. I have already given you several examples, and there are many, many more; how, given the situation, by changing the way I looked at it, I converted what was apparently a defect to an asset. I'll give you another example. I am an egotistical person; there is no doubt about it. I knew that most people who took a sabbatical to write a book, didn't finish it on time. So before I left, I told all my friends that when I come back, that book was going to be done! Yes, I would have it done - I'd have been ashamed to come back without it! I used my ego to make myself behave the way I wanted to. I bragged about something so I'd have to perform. I found out many times, like a cornered rat in a real trap, I was surprisingly capable. I have found that it paid to say, ``Oh yes, I'll get the answer for you Tuesday,'' not having any idea how to do it. By Sunday night I was really hard thinking on how I was going to deliver by Tuesday. I often put my pride on the line and sometimes I failed, but as I said, like a cornered rat I'm surprised how often I did a good job. I think you need to learn to use yourself. I think you need to know how to convert a situation from one view to another which would increase the chance of success.

Now self-delusion in humans is very, very common. There are enumerable ways of you changing a thing and kidding yourself and making it look some other way. When you ask, ``Why didn't you do such and such,'' the person has a thousand alibis. If you look at the history of science, usually these days there are 10 people right there ready, and we pay off for the person who is there first. The other nine fellows say, ``Well, I had the idea but I didn't do it and so on and so on.'' There are so many alibis. Why weren't you first? Why didn't you do it right? Don't try an alibi. Don't try and kid yourself. You can tell other people all the alibis you want. I don't mind. But to yourself try to be honest.

If you really want to be a first-class scientist you need to know yourself, your weaknesses, your strengths, and your bad faults, like my egotism. How can you convert a fault to an asset? How can you convert a situation where you haven't got enough manpower to move into a direction when that's exactly what you need to do? I say again that I have seen, as I studied the history, the successful scientist changed the viewpoint and what was a defect became an asset.

In summary, I claim that some of the reasons why so many people who have greatness within their grasp don't succeed are: they don't work on important problems, they don't become emotionally involved, they don't try and change what is difficult to some other situation which is easily done but is still important, and they keep giving themselves alibis why they don't. They keep saying that it is a matter of luck. I've told you how easy it is; furthermore I've told you how to reform. Therefore, go forth and become great scientists!

DISCUSSION - QUESTIONS AND ANSWERS

A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and observations accumulated over a fantastic career; I lost track of all the observations that were striking home. Some of them are very very timely. One was the plea for more computer capacity; I was hearing nothing but that this morning from several people, over and over again. So that was right on the mark today even though here we are 20 - 30 years after when you were making similar remarks, Dick. I can think of all sorts of lessons that all of us can draw from your talk. And for one, as I walk around the halls in the future I hope I won't see as many closed doors in Bellcore. That was one observation I thought was very intriguing.

Thank you very, very much indeed Dick; that was a wonderful recollection. I'll now open it up for questions. I'm sure there are many people who would like to take up on some of the points that Dick was making.

Hamming: First let me respond to Alan Chynoweth about computing. I had computing in research and for 10 years I kept telling my management, ``Get that !&@#% machine out of research. We are being forced to run problems all the time. We can't do research because were too busy operating and running the computing machines.'' Finally the message got through. They were going to move computing out of research to someplace else. I was persona non grata to say the least and I was surprised that people didn't kick my shins because everybody was having their toy taken away from them. I went in to Ed David's office and said, ``Look Ed, you've got to give your researchers a machine. If you give them a great big machine, we'll be back in the same trouble we were before, so busy keeping it going we can't think. Give them the smallest machine you can because they are very able people. They will learn how to do things on a small machine instead of mass computing.'' As far as I'm concerned, that's how UNIX arose. We gave them a moderately small machine and they decided to make it do great things. They had to come up with a system to do it on. It is called UNIX!

A. G. Chynoweth: I just have to pick up on that one. In our present environment, Dick, while we wrestle with some of the red tape attributed to, or required by, the regulators, there is one quote that one exasperated AVP came up with and I've used it over and over again. He growled that, ``UNIX was never a deliverable!''

Question: What about personal stress? Does that seem to make a difference?

Hamming: Yes, it does. If you don't get emotionally involved, it doesn't. I had incipient ulcers most of the years that I was at Bell Labs. I have since gone off to the Naval Postgraduate School and laid back somewhat, and now my health is much better. But if you want to be a great scientist you're going to have to put up with stress. You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said. If you want to lead a nice happy life with a lot of recreation and everything else, you'll lead a nice life.

Question: The remarks about having courage, no one could argue with; but those of us who have gray hairs or who are well established don't have to worry too much. But what I sense among the young people these days is a real concern over the risk taking in a highly competitive environment. Do you have any words of wisdom on this?

Hamming: I'll quote Ed David more. Ed David was concerned about the general loss of nerve in our society. It does seem to me that we've gone through various periods. Coming out of the war, coming out of Los Alamos where we built the bomb, coming out of building the radars and so on, there came into the mathematics department, and the research area, a group of people with a lot of guts. They've just seen things done; they've just won a war which was fantastic. We had reasons for having courage and therefore we did a great deal. I can't arrange that situation to do it again. I cannot blame the present generation for not having it, but I agree with what you say; I just cannot attach blame to it. It doesn't seem to me they have the desire for greatness; they lack the courage to do it. But we had, because we were in a favorable circumstance to have it; we just came through a tremendously successful war. In the war we were looking very, very bad for a long while; it was a very desperate struggle as you well know. And our success, I think, gave us courage and self confidence; that's why you see, beginning in the late forties through the fifties, a tremendous productivity at the labs which was stimulated from the earlier times. Because many of us were earlier forced to learn other things - we were forced to learn the things we didn't want to learn, we were forced to have an open door - and then we could exploit those things we learned. It is true, and I can't do anything about it; I cannot blame the present generation either. It's just a fact.

Question: Is there something management could or should do?

Hamming: Management can do very little. If you want to talk about managing research, that's a totally different talk. I'd take another hour doing that. This talk is about how the individual gets very successful research done in spite of anything the management does or in spite of any other opposition. And how do you do it? Just as I observe people doing it. It's just that simple and that hard!

Question: Is brainstorming a daily process?

Hamming: Once that was a very popular thing, but it seems not to have paid off. For myself I find it desirable to talk to other people; but a session of brainstorming is seldom worthwhile. I do go in to strictly talk to somebody and say, ``Look, I think there has to be something here. Here's what I think I see ...'' and then begin talking back and forth. But you want to pick capable people. To use another analogy, you know the idea called the `critical mass.' If you have enough stuff you have critical mass. There is also the idea I used to call `sound absorbers'. When you get too many sound absorbers, you give out an idea and they merely say, ``Yes, yes, yes.'' What you want to do is get that critical mass in action; ``Yes, that reminds me of so and so,'' or, ``Have you thought about that or this?'' When you talk to other people, you want to get rid of those sound absorbers who are nice people but merely say, ``Oh yes,'' and to find those who will stimulate you right back.

For example, you couldn't talk to John Pierce without being stimulated very quickly. There were a group of other people I used to talk with. For example there was Ed Gilbert; I used to go down to his office regularly and ask him questions and listen and come back stimulated. I picked my people carefully with whom I did or whom I didn't brainstorm because the sound absorbers are a curse. They are just nice guys; they fill the whole space and they contribute nothing except they absorb ideas and the new ideas just die away instead of echoing on. Yes, I find it necessary to talk to people. I think people with closed doors fail to do this so they fail to get their ideas sharpened, such as ``Did you ever notice something over here?'' I never knew anything about it - I can go over and look. Somebody points the way. On my visit here, I have already found several books that I must read when I get home. I talk to people and ask questions when I think they can answer me and give me clues that I do not know about. I go out and look!

Question: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?

Hamming: I believed, in my early days, that you should spend at least as much time in the polish and presentation as you did in the original research. Now at least 50% of the time must go for the presentation. It's a big, big number.

Question: How much effort should go into library work?

Hamming: It depends upon the field. I will say this about it. There was a fellow at Bell Labs, a very, very, smart guy. He was always in the library; he read everything. If you wanted references, you went to him and he gave you all kinds of references. But in the middle of forming these theories, I formed a proposition: there would be no effect named after him in the long run. He is now retired from Bell Labs and is an Adjunct Professor. He was very valuable; I'm not questioning that. He wrote some very good Physical Review articles; but there's no effect named after him because he read too much. If you read all the time what other people have done you will think the way they thought. If you want to think new thoughts that are different, then do what a lot of creative people do - get the problem reasonably clear and then refuse to look at any answers until you've thought the problem through carefully how you would do it, how you could slightly change the problem to be the correct one. So yes, you need to keep up. You need to keep up more to find out what the problems are than to read to find the solutions. The reading is necessary to know what is going on and what is possible. But reading to get the solutions does not seem to be the way to do great research. So I'll give you two answers. You read; but it is not the amount, it is the way you read that counts.

Question: How do you get your name attached to things?

Hamming: By doing great work. I'll tell you the hamming window one. I had given Tukey a hard time, quite a few times, and I got a phone call from him from Princeton to me at Murray Hill. I knew that he was writing up power spectra and he asked me if I would mind if he called a certain window a ``Hamming window.'' And I said to him, ``Come on, John; you know perfectly well I did only a small part of the work but you also did a lot.'' He said, ``Yes, Hamming, but you contributed a lot of small things; you're entitled to some credit.'' So he called it the hamming window. Now, let me go on. I had twitted John frequently about true greatness. I said true greatness is when your name is like ampere, watt, and fourier - when it's spelled with a lower case letter. That's how the hamming window came about.

Question: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?

Hamming: In the short-haul, papers are very important if you want to stimulate someone tomorrow. If you want to get recognition long-haul, it seems to me writing books is more contribution because most of us need orientation. In this day of practically infinite knowledge, we need orientation to find our way. Let me tell you what infinite knowledge is. Since from the time of Newton to now, we have come close to doubling knowledge every 17 years, more or less. And we cope with that, essentially, by specialization. In the next 340 years at that rate, there will be 20 doublings, i.e. a million, and there will be a million fields of specialty for every one field now. It isn't going to happen. The present growth of knowledge will choke itself off until we get different tools. I believe that books which try to digest, coordinate, get rid of the duplication, get rid of the less fruitful methods and present the underlying ideas clearly of what we know now, will be the things the future generations will value. Public talks are necessary; private talks are necessary; written papers are necessary. But I am inclined to believe that, in the long-haul, books which leave out what's not essential are more important than books which tell you everything because you don't want to know everything. I don't want to know that much about penguins is the usual reply. You just want to know the essence.

Question: You mentioned the problem of the Nobel Prize and the subsequent notoriety of what was done to some of the careers. Isn't that kind of a much more broad problem of fame? What can one do?

Hamming: Some things you could do are the following. Somewhere around every seven years make a significant, if not complete, shift in your field. Thus, I shifted from numerical analysis, to hardware, to software, and so on, periodically, because you tend to use up your ideas. When you go to a new field, you have to start over as a baby. You are no longer the big mukity muk and you can start back there and you can start planting those acorns which will become the giant oaks. Shannon, I believe, ruined himself. In fact when he left Bell Labs, I said, ``That's the end of Shannon's scientific career.'' I received a lot of flak from my friends who said that Shannon was just as smart as ever. I said, ``Yes, he'll be just as smart, but that's the end of his scientific career,'' and I truly believe it was.

You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby. I'm not saying that you shift from music to theoretical physics to English literature; I mean within your field you should shift areas so that you don't go stale. You couldn't get away with forcing a change every seven years, but if you could, I would require a condition for doing research, being that you will change your field of research every seven years with a reasonable definition of what it means, or at the end of 10 years, management has the right to compel you to change. I would insist on a change because I'm serious. What happens to the old fellows is that they get a technique going; they keep on using it. They were marching in that direction which was right then, but the world changes. There's the new direction; but the old fellows are still marching in their former direction.

You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, ``Yes, I will give up my great reputation.'' For example, when error correcting codes were well launched, having these theories, I said, ``Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that.'' I deliberately refused to go on in that field. I wouldn't even read papers to try to force myself to have a chance to do something else. I managed myself, which is what I'm preaching in this whole talk. Knowing many of my own faults, I manage myself. I have a lot of faults, so I've got a lot of problems, i.e. a lot of possibilities of management.

Question: Would you compare research and management?

Hamming: If you want to be a great researcher, you won't make it being president of the company. If you want to be president of the company, that's another thing. I'm not against being president of the company. I just don't want to be. I think Ian Ross does a good job as President of Bell Labs. I'm not against it; but you have to be clear on what you want. Furthermore, when you're young, you may have picked wanting to be a great scientist, but as you live longer, you may change your mind. For instance, I went to my boss, Bode, one day and said, ``Why did you ever become department head? Why didn't you just be a good scientist?'' He said, ``Hamming, I had a vision of what mathematics should be in Bell Laboratories. And I saw if that vision was going to be realized, I had to make it happen; I had to be department head.'' When your vision of what you want to do is what you can do single-handedly, then you should pursue it. The day your vision, what you think needs to be done, is bigger than what you can do single-handedly, then you have to move toward management. And the bigger the vision is, the farther in management you have to go. If you have a vision of what the whole laboratory should be, or the whole Bell System, you have to get there to make it happen. You can't make it happen from the bottom very easily. It depends upon what goals and what desires you have. And as they change in life, you have to be prepared to change. I chose to avoid management because I preferred to do what I could do single-handedly. But that's the choice that I made, and it is biased. Each person is entitled to their choice. Keep an open mind. But when you do choose a path, for heaven's sake be aware of what you have done and the choice you have made. Don't try to do both sides.

Question: How important is one's own expectation or how important is it to be in a group or surrounded by people who expect great work from you?

Hamming: At Bell Labs everyone expected good work from me - it was a big help. Everybody expects you to do a good job, so you do, if you've got pride. I think it's very valuable to have first-class people around. I sought out the best people. The moment that physics table lost the best people, I left. The moment I saw that the same was true of the chemistry table, I left. I tried to go with people who had great ability so I could learn from them and who would expect great results out of me. By deliberately managing myself, I think I did much better than laissez faire.

Question: You, at the outset of your talk, minimized or played down luck; but you seemed also to gloss over the circumstances that got you to Los Alamos, that got you to Chicago, that got you to Bell Laboratories.

Hamming: There was some luck. On the other hand I don't know the alternate branches. Until you can say that the other branches would not have been equally or more successful, I can't say. Is it luck the particular thing you do? For example, when I met Feynman at Los Alamos, I knew he was going to get a Nobel Prize. I didn't know what for. But I knew darn well he was going to do great work. No matter what directions came up in the future, this man would do great work. And sure enough, he did do great work. It isn't that you only do a little great work at this circumstance and that was luck, there are many opportunities sooner or later. There are a whole pail full of opportunities, of which, if you're in this situation, you seize one and you're great over there instead of over here. There is an element of luck, yes and no. Luck favors a prepared mind; luck favors a prepared person. It is not guaranteed; I don't guarantee success as being absolutely certain. I'd say luck changes the odds, but there is some definite control on the part of the individual.

Go forth, then, and do great work!

2024-07-06 16:58:27