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你和你的研究，理查德·漢明 （Richard Hamming）

理查德·漢明（Richard Hamming）在1986年3月發表了這次演講。[1] 這是我讀過的最好的演講之一，長期以來一直影響著我對如何度過時間的看法。

這個周末，我向一些人提到了它，令我驚訝的是，他們從未聽說過它。所以我雖然我會在這里分享它：

[23 年 5 月 28 日補充：請參閱 Gwern 的這個很棒的注釋版本。

很高興來到這里。我懷疑我是否能不辜負介紹。我演講的題目是“你和你的研究”。這不是關于管理研究，而是關于你個人如何進行研究。我可以就另一個主題發表演講——但不是，而是關于你。我不是在談論普通的普通研究;我說的是偉大的研究。為了描述偉大的研究，我偶爾會說諾貝爾獎類型的工作。它不一定要獲得諾貝爾獎，但我指的是那些我們認為是重要的事情。相對論，如果你愿意的話，香農的信息論，任何數量的杰出理論——這就是我正在談論的那種東西。

現在，我是怎么開始做這項研究的？在洛斯阿拉莫斯，我被請來運行其他人已經開始使用的計算機，這樣那些科學家和物理學家就可以重新開始工作。我看到我是個傀儡。我看到，雖然身體上是一樣的，但他們是不同的。說白了，我很羨慕。我想知道為什么他們與我如此不同。我近距離地看到了費曼。我看到了費米和泰勒。我看到了奧本海默。我見到了漢斯·貝特：他是我的老板。我見過不少非常有能力的人。我開始對那些這樣做的人和那些可能已經這樣做的人之間的區別非常感興趣。

當我來到貝爾實驗室時，我進入了一個非常高效的部門。博德當時是部門負責人;香農在那里，還有其他人。我繼續研究這些問題，“為什么？”和“有什么區別？”。隨后，我繼續閱讀傳記、自傳，問人們一些問題，比如：“你是怎么來的？我試圖找出有什么區別。這就是這次演講的意義所在。

那么，為什么這次演講很重要呢？我認為這很重要，因為據我所知，你們每個人都有一次生命。即使你相信輪回，它對你從一世到下一世也沒有任何好處！為什么你不應該在這一生中做有意義的事情，無論你如何定義重要？我不打算定義它——你知道我的意思。我將主要談論科學，因為這是我所研究的。但據我所知，其他人也告訴我，我所說的大部分內容適用于許多領域。在大多數領域，杰出的工作都具有非常相似的特征，但我將自己局限于科學。

為了單獨了解你，我必須用第一人稱說話。我必須讓你放下謙虛，對自己說，'是的，我想做一流的工作。我們的社會對那些真正致力于做好工作的人不屑一顧。你不應該這樣做;運氣應該降臨在你身上，你偶然做偉大的事情。嗯，這有點傻。我說，你為什么不著手做一些有意義的事情。你不必告訴別人，但你不應該對自己說，“是的，我想做一些有意義的事情。

為了進入第二階段，我必須放下謙虛，用第一人稱談論我所看到的，我做了什么，我聽到了什么。我要談談一些人，其中一些你認識，我相信當我們離開時，你不會引用我說的一些話。

讓我不是從邏輯上開始，而是從心理上開始。我發現主要的反對意見是，人們認為偉大的科學是靠運氣完成的。這完全是運氣問題。好吧，考慮一下愛因斯坦。注意他做了多少不同的事情是好的。都是運氣嗎？是不是有點太重復了？以香農為例。他不只是做信息論。幾年前，他做了一些其他的好事，還有一些仍然被鎖在密碼學的安全性中。他做了很多好事。

你一次又一次地看到，一個好人不僅僅是一件事。偶爾一個人一生只做一件事，我們稍后會談到，但很多時候是重復的。我聲稱運氣不會涵蓋一切。我要引用巴斯德的一句話，“運氣眷顧有準備的頭腦。我認為這和我所相信的一樣。確實有運氣的成分，不，沒有。有準備的頭腦遲早會發現一些重要的事情并去做。所以是的，這是運氣。你做的特別的事情是運氣，但你做某事不是。

例如，當我來到貝爾實驗室時，我和香農共用一個辦公室一段時間。與此同時，他在做信息論，我在做編碼理論。令人懷疑的是，我們兩個人在同一地點同時做到了——那是在大氣層中。你可以說，'是的，這是運氣。另一方面，你可以說，“但是為什么貝爾實驗室的所有人中只有兩個人這樣做了呢？是的，部分是運氣，部分是有準備的頭腦;但“部分”是我要談論的另一件事。所以，雖然我會再來幾次運氣，但我想把運氣這個問題作為你是否做得好的唯一標準。我聲稱你對它有一些控制權，但不是完全控制。最后，我將引用牛頓關于這個問題的話。牛頓說：“如果其他人能像我一樣努力思考，那么他們也會得到類似的結果。

你所看到的一個特征，包括偉大的科學家在內的許多人都有，是通常在他們年輕的時候，他們有獨立的思想，并有勇氣去追求它們。例如，愛因斯坦在12或14歲左右的時候問自己一個問題，“如果我用光速去看光波，它會是什么樣子？現在他知道電磁理論說你不能有一個平穩的局部最大值。但是，如果他隨著光速移動，他會看到一個局部最大值。他在12歲、14歲或那里的某個地方看到了一個矛盾，一切都不對勁，光速有一些特殊的東西。他最終創造了狹義相對論是幸運嗎？在早期，他通過思考碎片來奠定一些碎片。這是必要條件，但不是充分條件。我要談的所有這些項目都是運氣而不是運氣。

擁有大量的“大腦”怎么樣？聽起來不錯。在座的大多數人可能有足夠的大腦來做一流的工作。但偉大的工作不僅僅是大腦。大腦的測量方式多種多樣。在數學、理論物理學、天體物理學中，通常大腦在很大程度上與操縱符號的能力相關。因此，典型的智商測試很容易給他們打得相當高。另一方面，在其他領域，情況就不同了。例如，比爾·普凡（Bill Pfann），那個做區域融化的人，有一天來到我的辦公室。他腦海中模糊地有這個想法，關于他想要什么，他有一些方程式。我很清楚，這個人不太懂數學，而且他不太善于表達。他的問題似乎很有趣，所以我把它帶回家做了一點工作。最后，我向他展示了如何運行計算機，這樣他就可以計算自己的答案。我給了他計算的能力。他繼續前進，得到了自己部門的認可，但最終他獲得了該領域的所有獎項。一旦他開始了良好的工作，他的害羞、笨拙、口齒不清就消失了，他在許多其他方面都變得更有效率了。當然，他變得更加善于表達。

我可以用同樣的方式引用另一個人。我相信他不在觀眾席上，即一個名叫克洛斯頓的家伙。我在約翰·皮爾斯（John Pierce）的團隊中處理一個問題時遇到了他，我認為他沒有太多。我問在學校里和他一起上學的朋友，“他在研究生院是這樣的嗎？ ”是的，“他們回答說。好吧，我本來會解雇這個家伙的，但 J. R. Pierce 很聰明，讓他繼續留任。Clogston 終于完成了 Clogston 電纜。在那之后，有源源不斷的好主意。一次成功給他帶來了信心和勇氣。

成功科學家的特征之一是有勇氣。一旦你鼓起勇氣，相信你可以做重要的問題，那么你就可以了。如果你認為你做不到，幾乎可以肯定你不會。勇氣是香農最常擁有的東西之一。你只需要想想他的大定理。他想創建一種編碼方法，但他不知道該怎么做，所以他做了一個隨機代碼。然后他被卡住了。然后他問了一個不可能的問題，“平均隨機碼會做什么？然后，他證明了平均代碼是任意好的，因此必須至少有一個好的代碼。除了一個有無限勇氣的人，誰敢去想這些想法呢？這是偉大科學家的特征;他們有勇氣。他們將在不可思議的情況下繼續前進;他們思考并繼續思考。

年齡是物理學家特別擔心的另一個因素。他們總是說，你必須在年輕的時候這樣做，否則你永遠不會這樣做。愛因斯坦很早就做了一些事情，所有的量子力學研究員在做最好的工作時都年輕得令人作嘔。大多數數學家、理論物理學家和天體物理學家在年輕時都會做我們認為最好的工作。不是他們晚年不做好事，而是我們最看重的往往是他們早年做的事。另一方面，在音樂、政治和文學方面，我們認為他們最好的作品往往完成得很晚。我不知道你所處的哪個領域如何符合這個規模，但年齡有一些影響。

但讓我說一下為什么年齡似乎有它的影響。首先，如果你做了一些好的工作，你會發現自己在各種委員會中，無法再做任何工作。你可能會發現自己就像我看到布拉坦獲得諾貝爾獎時一樣。宣布獲獎的那天，我們都聚集在阿諾德禮堂;三位獲獎者都起身致辭。第三位是布拉坦，他幾乎眼里含著淚水，他說：“我知道諾貝爾獎的影響，我不會讓它影響我;我將保持老沃爾特·布拉坦（Walter Brattain）的好狀態。我對自己說，'那很好。但幾周后，我發現它正在影響他。現在他只能解決大問題。

當你出名時，很難解決小問題。這就是香農的所作所為。在信息論之后，你為安可做什么？偉大的科學家經常犯這個錯誤。他們未能繼續種植小橡子，強大的橡樹就是從這些橡子中生長出來的。他們試圖把大事搞定。但事實并非如此。所以這就是為什么你發現當你得到早期認可時，它似乎會讓你絕育的另一個原因。事實上，我會給你多年來我最喜歡的一句話。在我看來，普林斯頓高等研究院毀掉的優秀科學家比任何機構創造的都多，根據他們來之前做了什么來判斷，根據他們來之后做了什么來判斷。并不是說他們后來不好，而是他們在到達那里之前是一流的，只有在他們之后才很好。

這帶來了一個話題，也許是無序的，工作條件。大多數人認為最好的工作條件，其實并非如此。很明顯，它們不是因為人們在工作條件惡劣時往往最有生產力。劍橋物理實驗室最好的時代之一就是他們幾乎擁有棚屋的時候——他們做了一些有史以來最好的物理學。

我給你講一個我自己私生活的故事。在早期，我就清楚地意識到，貝爾實驗室不會給我傳統的編程人員，讓我以絕對二進制的方式對計算機進行編程。很明顯，他們不會這樣做。但每個人都是這樣做的。我可以毫不費力地去西海岸，在飛機公司找到一份工作，但令人興奮的人在貝爾實驗室，而飛機公司的人卻沒有。我想了很久，“我是否想去？”我想知道我怎樣才能從兩個可能的世界中獲得最好的結果。我最后對自己說，'漢明，你認為機器幾乎可以做任何事情。為什么你不能讓他們寫程序呢？起初在我看來是一個缺陷，迫使我很早就開始自動編程。看似錯誤的東西，通常，通過觀點的改變，被證明是你能擁有的最大資產之一。但是，當你第一次看到這個東西時，你不太可能認為，“哎呀，我永遠不會得到足夠的程序員，所以我怎么能做任何偉大的編程呢？

還有許多其他同類故事;格蕾絲·霍珀（Grace Hopper）也有類似的。我認為，如果你仔細觀察，你會發現，偉大的科學家往往通過把問題轉過來，把一個缺陷變成了一個資產。例如，許多科學家在發現自己做不到一個問題時，最終開始研究為什么不做。然后他們把它反過來說，“當然，這就是它”，并得到了一個重要的結果。所以理想的工作條件很奇怪。你想要的并不總是最適合你的。

現在是驅動問題。你觀察到，大多數偉大的科學家都有巨大的動力。我在貝爾實驗室與約翰·圖基（John Tukey）共事了十年。他有巨大的動力。在我加入大約三四年后的一天，我發現約翰·圖基比我年輕一點。約翰是個天才，而我顯然不是。我沖進博德的辦公室，問道，“我這個年紀的人怎么能像約翰·圖基那樣知道那么多呢？他靠在椅子上，雙手放在腦后，微微一笑，說：“你會驚訝的，漢明，如果你像他那樣努力工作那么多年，你會知道多少。我只是溜出辦公室！

博德的意思是：“知識和生產力就像復利。假設兩個能力大致相同的人，一個人的工作量比另一個人多百分之十，后者的產量將比前者高出兩倍以上。你知道的越多，你學到的就越多;你學得越多，你能做的就越多;你能做的越多，機會就越多——這很像復利。我不想給你一個費率，但這是一個非常高的費率。如果兩個人的能力完全相同，那么一個日復一日地管理以多思考一個小時的人將在一生中大大提高工作效率。我把博德的話記在心里;幾年來，我花了很多時間試圖更努力地工作，我發現，事實上，我可以完成更多的工作。我不喜歡在我妻子面前說這句話，但有時我確實有點忽視了她;我需要學習。如果你打算完成你想做的事情，你必須忽略一些事情。這是毫無疑問的。

關于驅動力，愛迪生說：“天才是99%的汗水和1%的靈感。他可能夸大其詞，但這個想法是，扎實的工作，穩步應用，會讓你出人意料地走得更遠。穩步應用的努力，多做一點工作，智能應用是什么。這就是問題所在;驅動器，誤用，不會帶你到任何地方。我經常在想，為什么我在貝爾實驗室的那么多好朋友，他們和我一樣努力工作，卻沒有那么多東西可以展示。努力的誤用是一個非常嚴重的問題。僅僅努力工作是不夠的——它必須明智地應用。

我想談談另一個特點;這種特質就是模棱兩可。我花了一段時間才發現它的重要性。大多數人喜歡相信某事是真的，也可能不是真的。偉大的科學家可以很好地容忍模棱兩可。他們相信這個理論足以繼續前進;他們對此表示懷疑，以至于注意到了錯誤和故障，因此他們可以挺身而出，創造新的替代理論。如果你相信太多，你永遠不會注意到缺陷;如果你懷疑太多，你就不會開始。它需要一個可愛的平衡。但大多數偉大的科學家都非常清楚為什么他們的理論是正確的，他們也很清楚一些不太合適的輕微不合，他們不會忘記它。達爾文在他的自傳中寫道，他發現有必要寫下每一條似乎與他的信念相矛盾的證據，否則它們就會從他的腦海中消失。當你發現明顯的缺陷時，你必須保持敏感并跟蹤這些事情，并密切關注如何解釋它們或如何改變理論以適應它們。這些往往是偉大的貢獻。偉大的貢獻很少是通過添加另一個小數位來完成的。歸根結底是一種情感承諾。大多數偉大的科學家都完全致力于解決他們的問題。那些不敬業的人很少能做出杰出的、一流的工作。

再說一遍，情感上的投入是不夠的。這顯然是一個必要條件。我想我可以告訴你原因。每個研究過創造力的人最終都會說，“創造力來自你的潛意識。不知何故，突然間，它就在那里。它只是出現。好吧，我們對潛意識知之甚少;但有一件事你很清楚，你的夢想也來自你的潛意識。而且你也知道，在相當程度上，你的夢想是對當天經歷的改造。如果你日復一日地深深地沉浸在一個話題中，你的潛意識除了解決你的問題之外別無他法。所以你在某個早晨醒來，或者某個下午醒來，答案就有了。對于那些不致力于解決當前問題的人來說，潛意識會在其他事情上犯錯，不會產生大的結果。因此，管理自己的方法是，當你遇到一個真正重要的問題時，不要讓其他任何事情成為你關注的中心——你把你的想法放在這個問題上。讓你的潛意識保持饑餓，這樣它就必須解決你的問題，這樣你就可以安然入睡，并在早上免費獲得答案。

Alan Chynoweth提到我曾經在物理桌上吃飯。我和數學家們一起吃飯，我發現我已經知道相當多的數學知識了;事實上，我并沒有學到太多東西。正如他所說，物理表是一個令人興奮的地方，但我認為他夸大了我的貢獻。聽 Shockley、Brattain、Bardeen、JB Johnson、Ken McKay 和其他人的演講非常有趣，我學到了很多東西。但不幸的是，諾貝爾獎來了，晉升來了，剩下的就是渣滓。沒有人想要剩下的東西。好吧，和他們一起吃飯是沒有用的！

在食堂的另一邊是一張化學桌。我曾與其中一位研究員戴夫·麥考爾（Dave McCall）共事過;此外，他當時正在向我們的秘書求愛。我走過去說，'你介意我加入你嗎？他們不能拒絕，所以我開始和他們一起吃了一段時間。我開始問，''你所在領域的重要問題是什么？大約一周后，“你在處理什么重要的問題？又過了一段時間，有一天我進來說，'如果你正在做的事情不重要，如果你認為它不會導致一些重要的事情，你為什么要在貝爾實驗室工作呢？在那之后，我不受歡迎;我得找別人一起吃飯！那是在春天。

秋天，戴夫·麥考爾（Dave McCall）在大廳里攔住了我，說：“漢明，你的那句話深深地打動了我的皮膚。我整個夏天都在思考這個問題，即我所在領域的重要問題是什么。我沒有改變我的研究，“他說，”但我認為這是非常值得的。我說，'謝謝你，戴夫，'然后繼續說。幾個月后，我注意到他被任命為部門負責人。前幾天我注意到他是美國國家工程院院士。我注意到他成功了。我從未聽說過在科學界和科學界提到那張桌子上任何其他研究員的名字。他們無法問自己，“我所在領域的重要問題是什么？

如果你不處理一個重要的問題，你就不太可能做重要的工作。這是顯而易見的。偉大的科學家已經仔細地思考了他們領域中的一些重要問題，他們一直在思考如何解決這些問題。讓我警告你，“重要問題”必須謹慎措辭。從某種意義上說，物理學中的三個懸而未決的問題，是我在貝爾實驗室工作時從未研究過的。我的意思是保證獲得諾貝爾獎和您想提及的任何金額。我們沒有研究（1）時間旅行，（2）瞬移，（3）反重力。它們不是重要的問題，因為我們沒有攻擊。使問題變得重要的不是結果，而是你有一個合理的攻擊。這就是問題的重要性所在。當我說大多數科學家不研究重要問題時，我的意思是在這個意義上。據我所知，一般的科學家幾乎把所有的時間都花在了他認為不重要的問題上，他也不相信這些問題會導致重要的問題。

我之前說過種植橡子，這樣橡樹就會生長。你不能總是確切地知道去哪里，但你可以在可能發生某些事情的地方保持活躍。即使你相信偉大的科學是運氣問題，你也可以站在閃電擊中的山頂上;你不必躲在你安全的山谷里。但是普通的科學家幾乎一直在做例行的安全工作，所以他（或她）的產量并不高。就是這么簡單。如果你想把工作做好，你顯然必須在重要的問題上下功夫，你應該有一個想法。

在約翰·圖基（John Tukey）和其他人的敦促下，我終于采用了我稱之為“偉大思想時間”（Great Thoughts Time）的方法。當我星期五中午去吃午飯時，我只會在那之后討論偉大的想法。我所說的偉大想法是指：“計算機在整個AT&T中扮演什么角色？”、“計算機將如何改變科學？””例如，我當時得出的結論是，十分之九的實驗是在實驗室完成的，十分之一的實驗是在計算機上完成的。有一次，我對副總統們說，這將是相反的，即十分之九的實驗將在計算機上完成，十分之一的實驗將在實驗室中完成。他們知道我是一個瘋狂的數學家，沒有現實感。我知道他們錯了，他們被證明是錯的，而我被證明是對的。當他們不需要實驗室時，他們就會建造實驗室。我看到計算機正在改變科學，因為我花了很多時間問“計算機將對科學產生什么影響，我該如何改變它？我問自己，''它將如何改變貝爾實驗室？我曾經在同一次演講中說過，在我離開之前，貝爾實驗室超過一半的人將與計算機密切互動。好吧，你們現在都有終端了。我認真思考我的領域將走向何方，機會在哪里，以及要做的事情是什么。讓我去那里，這樣我就有機會做一些重要的事情。

大多數偉大的科學家都知道許多重要的問題。他們有 10 到 20 個重要問題，他們正在尋找攻擊。當他們看到一個新想法出現時，人們會聽到他們說：“嗯，這與這個問題有關。他們放下所有其他東西并追逐它。現在我可以告訴你一個告訴我的恐怖故事，但我不能保證它的真實性。我坐在機場里和我一個來自洛斯阿拉莫斯的朋友聊天，說裂變實驗在歐洲發生是多么幸運，因為這讓我們在美國的原子彈上工作。他說：''不;在伯克利，我們收集了一堆數據;我們沒有辦法減少它，因為我們正在建造更多的設備，但如果我們減少這些數據，我們就會發現裂變。他們手里拿著它，他們沒有追求它。他們排在第二位！

偉大的科學家，當機會出現時，他們會去追求它，并追求它。他們放棄了所有其他東西。他們擺脫了其他東西，他們追求一個想法，因為他們已經把事情想清楚了。他們的思想已經準備好了;他們看到了機會，并去追逐它。當然，很多時候它并不奏效，但你不必擊中他們中的許多人來做一些偉大的科學研究。這很容易。主要技巧之一就是長壽！

另一個特征，我花了一段時間才注意到。我注意到以下關于在門打開或關門的情況下工作的人的事實。我注意到，如果你把辦公室的門關上，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數人都高。但 10 年后，不知何故，你不知道什么問題值得努力;你所做的所有辛勤工作在重要性上都是無關緊要的。開著門工作的人會受到各種干擾，但他偶爾也會得到關于世界是什么以及什么是重要的線索。現在我無法證明因果順序，因為你可能會說，「關閉的門象徵著一個關閉的心靈。我不知道。但我可以說，那些敞開大門工作的人和那些最終做重要事情的人之間有很好的相關性，盡管那些關著門工作的人往往更努力地工作。不知何故，他們似乎在做一件稍微錯誤的事情——不多，但足以讓他們錯過名聲。

我想談談另一個話題。它基于我想你們很多人都知道的那首歌，“這不是你做什么，而是你做的方式。我將從我自己的例子開始。在絕對二進制的日子里，我被騙到在數字計算機上做，這是最好的模擬計算機無法解決的問題。我得到了答案。當我仔細想了想，對自己說，'你知道，漢明，你將不得不提交一份關于這項軍事工作的報告;在你花了很多錢之后，你將不得不考慮它，每個模擬安裝都會希望報告看看他們是否找不到其中的缺陷。至少可以說，我正在用一種相當糟糕的方法進行所需的集成，但我得到了答案。我意識到，事實上，問題不僅僅是得到答案;這是第一次，毫無疑問，我可以用數字機器在自己的地面上擊敗模擬計算機。我重新設計了求解方法，創造了一個漂亮而優雅的理論，并改變了我們計算答案的方式;結果沒有什么不同。發表的報告有一種優雅的方法，后來被稱為“漢明積分微分方程的方法”。它現在有點過時了，但有一段時間它是一種非常好的方法。通過稍微改變問題，我做了重要的工作，而不是瑣碎的工作。

同樣，早期在閣樓上使用機器時，我正在解決一個又一個問題;相當多的人是成功的，也有一些失敗。一個星期五，我做完一道題后回家了，奇怪的是，我并不開心;我很郁悶。我可以看到生活是一個接一個問題的長序列。經過一段時間的思考，我決定，“不，我應該大規模生產可變產品。我應該關心明年的所有問題，而不僅僅是我面前的問題。通過改變問題，我仍然得到了同樣或更好的結果，但我改變了事情并做了重要的工作。我解決了一個主要問題——當我不知道它們會是什么時，我如何征服機器并解決明年的所有問題？我該如何準備？我該怎么做才能掌握它？我如何遵守牛頓法則？他說：“如果我比別人看得更遠，那是因為我站在巨人的肩膀上。這些天我們站在彼此的腳上！

你應該以這樣一種方式做你的工作，讓其他人可以在它的基礎上建立起來，所以他們確實會說，“是的，我站在某某的肩膀上，我看得更遠。科學的本質是累積的。通過稍微改變一個問題，你通常可以做偉大的工作，而不僅僅是好的工作。我沒有攻擊孤立的問題，而是下定決心，我永遠不會再解決孤立的問題，除非作為類的特征。

現在，如果你是一個數學家，你就會知道，推廣的努力通常意味著解決方案很簡單。經常停下來說，“這是他想要的問題，但這是某某的特征。是的，我可以用比特定方法優越得多的方法攻擊整個班級，因為我之前被嵌入了不必要的細節。抽象業務經常使事情變得簡單。此外，我把方法歸檔，為未來的問題做好準備。

在結束這一部分時，我會提醒你，“這是一個可憐的工人責怪他的工具——好人繼續工作，考慮到他所擁有的，并得到他所能得到的最好的答案。我建議，通過改變問題，通過以不同的方式看待事物，你可以對你的最終生產力產生很大的影響，因為你可以以這樣一種方式去做，人們確實可以在你做過的事情上再接再厲，或者你可以用這樣一種方式去做，讓下一個人不得不再次復制你做過的事情。這不僅僅是工作的問題，而是你寫報告的方式，你寫論文的方式，整個態度。做一個廣泛的、一般的工作，就像做一個非常特殊的案例一樣容易。而且它更令人滿意和有益！

我現在來談談一個非常令人反感的話題;僅僅做一份工作是不夠的，你必須賣掉它。“推銷”給科學家是一件尷尬的事情。它非常丑陋;你不應該這樣做。世界應該在等待，當你做一些偉大的事情時，他們應該沖出來歡迎它。但事實是，每個人都忙于自己的工作。你必須把它呈現得如此之好，以至于他們會把他們正在做的事情放在一邊，看看你做了什么，讀一讀，然后回來說，“是的，這很好。我建議，當你打開一本日記時，當你翻頁時，你會問為什么你讀一些文章而不是其他文章。你最好寫你的報告，這樣當它發表在《物理評論》上時，或者你想要的任何地方，當讀者翻頁時，他們不僅會翻你的頁面，而且會停下來閱讀你的頁面。如果他們不停下來閱讀它，你就不會得到學分。

在銷售中，您必須做三件事。你必須學會寫得清楚好，這樣人們才能讀懂它，你必須學會進行合理的正式演講，你還必須學會進行非正式的演講。我們有很多所謂的“幕后科學家”。在會議上，他們會保持沉默。三周后，在做出決定后，他們提交了一份報告，說明你為什么要這樣做。好吧，為時已晚。他們不會在激烈的會議中，在活動的中間站起來說，“出于這些原因，我們應該這樣做。你需要掌握這種溝通形式以及準備好的演講。

剛開始演講時，我的身體幾乎生病了，我非常非常緊張。我意識到我要么必須學會順利發表演講，否則我基本上會部分癱瘓我的整個職業生涯。有一天晚上，IBM第一次邀請我在紐約發表演講，我決定要做一個非常好的演講，一個需要的演講，不是技術性的演講，而是廣泛的演講，最后如果他們喜歡，我會悄悄地說，“只要你想要一個，我就會進來給你一個。結果，我得到了大量的練習，向有限的聽眾發表演講，我克服了害怕。此外，我還可以研究哪些方法是有效的，哪些是無效的。

在參加會議時，我已經在研究為什么有些論文被記住了，而大多數論文卻沒有被記住。技術人員想做一個非常有限的技術演講。大多數時候，聽眾想要一個廣泛的一般性演講，并且想要比演講者愿意提供的更多的調查和背景。結果，許多談判都是無效的。演講者說出一個主題，然后突然投入到他所解決的細節中。觀眾中很少有人會跟隨。你應該畫一幅大致的圖景，說明為什么它很重要，然后慢慢地給出一個草圖。然后更多的人會說，“是的，喬做到了，”或者“瑪麗做到了;我真的看到它在哪里;是的，瑪麗真的講得很好;我明白瑪麗的所作所為。傾向于進行高度限制的、安全的談話;這通常是無效的。此外，許多演講都充滿了太多的信息。所以我說這種銷售的想法是顯而易見的。

讓我總結一下。你必須解決重要的問題。我否認這都是運氣，但我承認運氣是有相當的成分。我同意巴斯德的“運氣眷顧有準備的頭腦”。我非常喜歡我所做的事情。多年來，周五下午——只有偉大的想法——意味著我花了 10% 的時間試圖理解該領域更大的問題，即什么是重要的，什么是不重要的。我發現在早期，我一直相信“這個”，但花了整整一周的時間朝著“那個”方向前進。這有點愚蠢。如果我真的相信行動已經結束了，我為什么要朝這個方向前進？我要么改變我的目標，要么改變我所做的事情。所以我改變了我所做的一些事情，我朝著我認為重要的方向前進。就這么簡單。

現在你可能會告訴我，你無法控制你必須做什么。好吧，當你第一次開始時，你可能不會。但是，一旦你取得了適度的成功，就會有更多的人要求結果，而不是你所能提供的，你有一些選擇的權力，但不是完全的。我給你講一個關于這個故事的故事，它與教育你的老板有關。我有一個名叫謝爾庫諾夫的老板;他曾經是，現在仍然是我的一個非常好的朋友。一些軍人來找我，要求在星期五之前給出一些答案。好吧，我已經將我的計算資源用于為一群科學家即時減少數據;我陷入了簡短、小而重要的問題。這位軍人希望我在周五結束前解決他的問題。我說，'不，我星期一給你。我可以在周末工作。我現在不打算這樣做了。他去找我的老板謝爾庫諾夫，謝爾庫諾夫說，'你必須為他管理這個;他必須在周五之前拿到它。我告訴他，''我為什么要這樣做？他說，“你必須這樣做。我說，“好吧，謝爾蓋，但是你星期五下午坐在辦公室里，趕上回家的晚班車，看著這個家伙走出那扇門。星期五下午晚些時候，我給了軍人答案。然后我去了謝爾庫諾夫的辦公室坐了下來;當那人出去時，我說，'你看謝爾庫諾夫，這家伙的胳膊下什么都沒有;但我給了他答案。星期一早上，謝爾庫諾夫打電話給他，說：“你周末來上班了嗎？我能聽到，好像，當那家伙在腦海中閃過將要發生的事情時，停頓了一下;但是他知道他必須登錄，而且他最好不要說他有，當他沒有的時候，所以他說他沒有。從那以后，謝爾庫諾夫說，“你設定了你的最后期限;你可以改變它們。

一個教訓足以讓我的老板知道，為什么我不想做取代探索性研究的大工作，以及為什么我有理由不做吸收所有研究計算設施的速成工作。相反，我想使用這些工具來計算大量小問題。同樣，在早期，我的計算能力有限，很明顯，在我所在的地區，“數學家對機器沒有用處”。但我需要更多的機器容量。每次我不得不告訴其他領域的科學家，“不，我不能;我沒有機器容量，“他抱怨道。我說，''去告訴你的副總統，漢明需要更多的計算能力。過了一會兒，我可以看到頂部發生了什么;許多人對我的副總統說，''你的人需要更多的計算能力。知道了！

我還做了第二件事。當我借出我們在計算早期所擁有的一點編程能力時，我說，“我們的程序員沒有得到他們應得的認可。當你發表一篇論文時，你會感謝那個程序員，否則你就不會再從我這里得到任何幫助。那位程序員將被點名感謝;她很努力。我等了幾年。然后，我瀏覽了一年的BSTJ文章，并計算了感謝某個程序員的比例。我把它拿給老板說，'這就是計算在貝爾實驗室發揮的核心作用;如果BSTJ很重要，那么計算就有多重要。他不得不屈服。你可以教育你的老板。這是一項艱巨的工作。在這次演講中，我只是從下往上看;我不是從上到下看的。但我告訴你，盡管有高層管理人員，你怎么能得到你想要的東西。你也必須在那里推銷你的想法。

好吧，我現在歸結為這個話題，“成為一名偉大科學家的努力值得嗎？要回答這個問題，你必須問人。當你超越他們的謙虛時，大多數人會說，“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樣好，”或者如果是一個女人，她說，“這就像酒、男人和歌加在一起一樣好。如果你看看老板們，他們往往會回來或要求報告，試圖參與那些發現的時刻。他們總是擋路。所以很明顯，那些已經做過的人，想再做一次。但這是一項有限的調查。我從來不敢出去問那些做得不好的人，他們對這件事有什么看法。這是一個有偏見的樣本，但我仍然認為這是值得奮斗的。我認為，努力去做一流的工作絕對是值得的，因為事實是，斗爭的價值大于結果。為自己做點什么而奮斗本身似乎是值得的。在我看來，成功和名聲是一種紅利。

我已經告訴過你怎么做。這很容易，那么為什么這么多人，盡管他們所有的才能，都失敗了？例如，直到今天，我的觀點是，在貝爾實驗室的數學系里，有不少人比我更有能力，更有天賦，但他們的產量卻沒有那么多。他們中的一些人確實比我生產得更多;香農的產量比我多，其他一些人也生產了很多，但我的生產力很高，與許多其他裝備更好的人相比。為什么會這樣？他們怎么了？為什么那么多有前途的人都失敗了？

嗯，原因之一是動力和承諾。那些能力較差但致力于此的人，比那些擁有高超技能并涉足它的人做得更多，他們白天工作，回家做其他事情，第二天回來工作。他們沒有真正一流的工作顯然需要的深刻承諾。他們做了很多好工作，但我們談論的是一流的工作，記住。這是有區別的。好人，非常有才華的人，幾乎總是能做出好工作。我們談論的是杰出的工作，獲得諾貝爾獎并得到認可的工作類型。

第二件事，我認為，是人格缺陷的問題。現在我要引用我在爾灣遇到的一個家伙。他曾是一個計算中心的負責人，他暫時被任命為大學校長的特別助理。很明顯，他有一份前途光明的工作。有一次，他帶我去他的辦公室，向我展示了他寫信的方法，以及他如何處理他的信件。他指出秘書的效率有多低。他把所有的信都堆在那里;他知道一切在哪里。他會用他的文字處理器把這封信拿出來。他吹噓這是多么了不起，以及他如何在沒有秘書干預的情況下完成如此多的工作。好吧，在他背后，我和秘書談了談。秘書說：“我當然幫不了他;我沒有收到他的郵件。他不會給我登錄的東西;我不知道他把它放在地板上的什么地方。我當然幫不了他。于是我去找他，說：'聽著，如果你采用現在的方法，做你單槍匹馬能做的事，你可以走那么遠，不會比你單槍匹馬能做的更遠。如果你學會了與系統合作，你可以在系統支持你的情況下走得更遠。而且，他再也沒有走得更遠。他有他的性格缺陷，想要完全控制，不愿意承認你需要系統的支持。

你發現這種情況一次又一次地發生;優秀的科學家會與系統作斗爭，而不是學會與系統合作并利用系統所提供的一切。如果你學會如何使用它，它有很多。這需要耐心，但你可以學習如何很好地使用這個系統，你可以學習如何繞過它。畢竟，如果你想要一個“不”的決定，你只需要去找你的老板，然后很容易地得到一個“不”。如果你想做某事，不要問，去做。向他展示一個既成的事實。不要給他機會告訴你“不”。但是，如果你想要一個“不”，很容易得到一個“不”。

另一個人格缺陷是自我主張，在這種情況下，我將談談我自己的經歷。我來自洛斯阿拉莫斯，早期我在紐約麥迪遜大道 590 號使用一臺機器，我們只是在那里租用時間。我仍然穿著西式服裝，大斜杠口袋，短褲和所有這些東西。我隱約注意到我沒有得到像其他人那樣好的服務。于是我開始測量。你進來了，你等著輪到你;我覺得我沒有得到公平的交易。我對自己說，'為什么？IBM沒有一個副總裁說過，“給漢明一個糟糕的時機”。是底層的秘書在做這件事。當一個插槽出現時，他們會急于找人溜進去，但他們出去找其他人。現在，為什么？我沒有虐待他們。回答，我沒有按照他們認為在這種情況下的人應該穿的衣服。歸根結底就是——我穿得不合適。我必須做出決定——我是要堅持我的自我，按照我想要的方式穿衣服，讓它不斷地耗盡我職業生涯的努力，還是我要看起來更符合要求？我決定要努力讓自己看起來符合要求。那一刻，我得到了更好的服務。而現在，作為一個老多彩的角色，我得到了比其他人更好的服務。

你應該根據聽眾的期望著裝。如果我要在麻省理工學院計算機中心提供地址，我會穿上一件短袍和一件舊的燈芯絨夾克或其他東西。我知道，我不會讓我的衣服、我的外表、我的舉止妨礙我所關心的事情。許多科學家認為他們必須堅持自己的自我，并以自己的方式做事。他們必須能夠做這個、那個或其他事情，并且他們付出穩定的價格。

約翰·圖基（John Tukey）幾乎總是穿著很隨意。他會進入一個重要的辦公室，過了很長時間，另一個人才意識到這是一個一流的人，他最好聽。很長一段時間以來，約翰不得不克服這種敵意。這是白費力氣！我沒有說你應該順從;我說：“順從的外表會讓你走得很遠。如果你選擇以任何方式維護你的自我，“我會按照我的方式去做”，那么你在整個職業生涯中都會付出一個小小的穩定代價。而這，在一生中，加起來就是大量不必要的麻煩。

通過不厭其煩地給秘書講笑話，并且有點友好，我得到了極好的秘書幫助。例如，有一次，出于某種愚蠢的原因，Murray Hill的所有復制服務都被捆綁了。不要問我怎么做，但他們是。我想做點什么。我的秘書打電話給霍姆德爾的某個人，跳上公司的車，走了一個小時的路，把它復制了下來，然后回來了。這是對我努力讓她振作起來、給她講笑話和保持友好的回報;正是這點額外的工作后來為我帶來了回報。通過意識到你必須使用這個系統并研究如何讓系統完成你的工作，你就學會了如何使系統適應你的愿望。或者你可以一輩子穩定地戰斗它，作為一場不宣而戰的小戰爭。

我認為約翰·圖基（John Tukey）付出了不必要的可怕代價。無論如何，他都是個天才，但我認為，如果他愿意順從一點，而不是自我主張，那會更好，也更簡單。他會一直按照自己想要的方式穿衣服。它不僅適用于著裝，也適用于其他一千件事情;人們將繼續與這個系統作斗爭。并不是說你不應該偶爾！

當他們把圖書館從墨累山的中間搬到遠端時，我的一個朋友提出了要自行車的要求。好吧，這個組織并不愚蠢。他們等了一會兒，發回了一張場地地圖，上面寫著：“請您在這張地圖上標明您將要走的路線，以便我們獲得涵蓋您的保險單。又過了幾個星期。然后他們問：“你打算把自行車存放在哪里，如何鎖上，這樣我們就可以這樣做。他終于意識到，他當然會被紅膠帶綁死，所以他屈服了。他升任貝爾實驗室總裁。

巴尼·奧利弗是個好人。他有一次給IEEE寫了一封信。當時貝爾實驗室的官方書架空間如此之大，IEEE論文集的高度也更大;由于你不能改變官方書架空間的大小，他給IEEE出版人寫了一封信，說：“既然有這么多IEEE成員在貝爾實驗室，而且官方空間如此之高，期刊的大小應該改變。他把它寄給老板簽字。回來的是一張帶有他簽名的碳，但他仍然不知道原件是否寄出。我并不是說你不應該做出改革的姿態。我是說，我對有能力的人的研究是，他們不會讓自己投入到那種戰爭中。他們玩了一會兒，然后放下它，繼續他們的工作。

許多二流的家伙陷入了對系統的一些小問題，并將其帶到了戰爭中。他把精力花在一個愚蠢的項目上。現在你要告訴我，必須有人改變這個系統。我同意;有人必須這樣做。你想成為哪個？是改變系統的人還是做一流科學的人？你想成為哪個人？要清楚，當你與系統作斗爭并與之斗爭時，你在做什么，在多大程度上擺脫娛樂，以及與系統作斗爭要浪費多少精力。我的建議是讓別人來做，然后你就可以成為一名一流的科學家。你們中很少有人有能力既改革制度又成為一流的科學家。

另一方面，我們不能總是屈服。有些時候，一定程度的叛逆是明智的。據我觀察，幾乎所有的科學家都喜歡在一定程度上對這個系統進行調侃，因為純粹是喜歡它。基本上可以歸結為，如果不在其他領域具有獨創性，您就無法在一個領域具有原創性。獨創性是不同的。如果沒有其他一些原創特征，你就不可能成為一個原創科學家。但是，許多科學家讓他在其他地方的怪癖使他付出了比他或她獲得的自我滿足所必需的更高的代價。我不反對所有的自我主張;我反對一些人。

另一個錯誤是憤怒。科學家經常會生氣，這是處理事情的方法。娛樂，是的，憤怒，不是。憤怒被誤導了。你應該跟隨和合作，而不是一直與系統作斗爭。

您應該尋找的另一件事是事物的積極一面，而不是消極的一面。我已經舉了幾個例子，還有很多很多的例子;鑒于這種情況，我如何通過改變我看待它的方式，將明顯的缺陷轉化為資產。我再舉一個例子。我是一個自負的人;這是毫無疑問的。我知道，大多數請假寫書的人，都沒有按時完成。所以在我離開之前，我告訴我所有的朋友，當我回來時，那本書就要完成了！是的，我會完成的——如果沒有它，我會很慚愧地回來！我用我的自我讓自己按照自己想要的方式行事。我吹噓了一些東西，所以我必須表演。我發現很多次，就像一只走投無路的老鼠在真正的陷阱里，我的能力出奇地好。我發現說“哦，是的，我會在星期二給你答案”，卻不知道該怎么做。到了星期天晚上，我真的很難想在周二之前我該如何交付。我經常把我的驕傲放在線上，有時我失敗了，但正如我所說，就像一只走投無路的老鼠一樣，我很驚訝我經常做得很好。我認為你需要學會使用自己。我認為你需要知道如何將情況從一種觀點轉換為另一種觀點，這將增加成功的機會。

現在人類的自欺欺人非常非常普遍。有無數種方法可以改變一件事，開玩笑，讓它看起來是另一種方式。當你問，“你為什么不做某某”時，這個人有一千個不在場證明。如果你看一下科學史，通常現在有 10 個人在那里準備好，我們為第一個在那里的人付出代價。其他九個人說，'嗯，我有這個想法，但我沒有去做，等等。有這么多不在場證明。你為什么不是第一個？你為什么不做對？不要嘗試不在場證明。不要試圖自欺欺人。你可以告訴其他人你想要的所有不在場證明。我不介意。但對你自己來說，試著說實話。

如果你真的想成為一名一流的科學家，你需要了解你自己，了解你的弱點，你的長處，以及你的缺點，就像我的自負一樣。如何將故障轉換為資產？你怎么能改變你沒有足夠的人力進入一個方向的情況，而這正是你需要做的？我再說一遍，當我研究歷史時，我看到成功的科學家改變了觀點，缺陷變成了資產。

總而言之，我聲稱，這么多擁有偉大成就的人沒有成功的一些原因是：他們不處理重要的問題，他們沒有在情感上投入，他們沒有嘗試將困難的事情改變為其他容易做到但仍然重要的情況，他們不斷給自己不在場證明為什么他們不這樣做。他們一直說這是運氣問題。我已經告訴過你這是多么容易;此外，我已經告訴過你如何改革。因此，勇往直前，成為偉大的科學家！

討論 - 問題和答案

A. G. Chynoweth：嗯，那是 50 分鐘的集中智慧和觀察，在一個夢幻般的職業生涯中積累起來;我忘記了所有令人震驚的觀察結果。其中一些非常非常及時。一個是請求增加計算機容量;今天早上，我一遍又一遍地從幾個人那里聽到這句話。所以今天這句話是正確的，盡管我們是在你發表類似言論的 20 到 30 年后，迪克。我能想到我們所有人都可以從你的演講中吸取的各種教訓。首先，當我將來在大廳里走來走去時，我希望我不會在 Bellcore 看到那么多緊閉的門。這是我認為非常有趣的一個觀察結果。

非常感謝你，迪克;那是一個美妙的回憶。我現在將打開它以供提問。我相信有很多人想接受迪克提出的一些觀點。

漢明：首先，讓我回答一下 Alan Chynoweth 關于計算的問題。我在研究中從事計算機工作，10 年來，我一直告訴我的管理層，“把那臺 ！&@#% 機器從研究中拿出來。我們一直被迫運行問題。我們無法進行研究，因為太忙于操作和運行計算機。最后，消息傳了出去。他們打算將計算從研究中轉移到其他地方。至少可以說，我是一個不受歡迎的人，我很驚訝人們沒有踢我的小腿，因為每個人都被拿走了他們的玩具。我走進艾德·戴維的辦公室，說，'聽著，艾德，你必須給你的研究人員一臺機器。如果你給他們一臺巨大的機器，我們就會回到以前的麻煩中，忙于讓它運轉，我們無法思考。給他們最小的機器，因為他們是非常能干的人。他們將學習如何在小型機器上做事，而不是大規模計算。就我而言，UNIX 就是這樣產生的。我們給了他們一臺中等大小的機器，他們決定讓它做偉大的事情。他們必須想出一個系統來做到這一點。它被稱為 UNIX！

A. G. Chynoweth：我只需要拿起那個。迪克，在我們目前的環境中，當我們與監管機構或監管機構要求的一些繁文縟節作斗爭時，有一句話是憤怒的 AVP 想出的，我一遍又一遍地使用它。他咆哮著說，“UNIX從來都不是可交付的！

問題：個人壓力呢？這似乎有什么不同嗎？

漢明：是的，確實如此。如果你沒有情感上的參與，它就不會。我在貝爾實驗室的大部分時間里都有早期潰瘍。從那以后，我去了海軍研究生院，稍微放松了一下，現在我的健康狀況好多了。但如果你想成為一名偉大的科學家，你就必須忍受壓力。你可以過上美好的生活;你可以是一個好人，也可以是一個偉大的科學家。但好人最后結束，是里奧·杜羅徹（Leo Durocher）說的。如果你想過上美好的幸福生活，有很多娛樂和其他一切，你就會過上美好的生活。

問題：關于有勇氣的言論，沒有人可以反駁;但是我們這些白發蒼蒼或地位高的人不必太擔心。但是，我現在的年輕人感覺到，在競爭激烈的環境中，對冒險的真正擔憂。你對此有什么智慧的話嗎？

漢明：我會更多地引用 Ed David 的話。埃德·戴維（Ed David）擔心我們社會中普遍失去神經。在我看來，我們確實經歷了不同的時期。從戰爭中走出來，從我們制造原子彈的洛斯阿拉莫斯走出來，從建造雷達等等走出來，進入了數學系和研究領域，一群很有膽量的人。他們剛剛看到事情已經完成;他們剛剛贏得了一場精彩的戰爭。我們有理由鼓起勇氣，因此我們做了很多事情。我不能安排這種情況再做一次。我不能責怪當代人沒有它，但我同意你說的;我只是不能責怪它。在我看來，他們沒有對偉大的渴望;他們缺乏這樣做的勇氣。但是我們有，因為我們處于有利的環境中擁有它;我們剛剛經歷了一場非常成功的戰爭。在戰爭中，我們在很長一段時間內看起來非常非常糟糕;正如你所知道的，這是一場非常絕望的斗爭。我認為，我們的成功給了我們勇氣和自信;這就是為什么你看到，從四十年代末到五十年代，實驗室的巨大生產力從早期就受到刺激。因為我們中的許多人以前被迫學習其他東西——我們被迫學習我們不想學習的東西，我們被迫敞開大門——然后我們可以利用我們學到的那些東西。這是真的，我對此無能為力;我也不能責怪當代人。這只是一個事實。

問題：管理層可以或應該做些什么嗎？

漢明：管理層能做的很少。如果你想談論管理研究，那是一個完全不同的談話。我還要花一個小時。這個演講是關于個人如何完成非常成功的研究，盡管管理層做了任何事情，或者盡管有任何其他反對意見。你是怎么做到的？就像我觀察人們這樣做一樣。就是這么簡單，就是這么難！

問題：頭腦風暴是一個日常過程嗎？

漢明：曾經這是一件非常受歡迎的事情，但似乎沒有得到回報。就我自己而言，我覺得與其他人交談是可取的;但是，頭腦風暴很少是值得的。我確實會嚴格地與某人交談，然后說，'看，我認為這里一定有什么東西。這是我想我看到的......”然后開始來回交談。但你想挑選有能力的人。再打個比方，你知道這個概念叫做“臨界質量”。如果你有足夠的東西，你就有臨界質量。還有一種我稱之為“吸音器”的想法。當你得到太多的吸音器時，你會給出一個想法，而他們只是說，“是的，是的，是的。你要做的是讓臨界質量付諸行動;“是的，這讓我想起了某某，”或者，“你有沒有想過那個或這個？當你和其他人交談時，你想擺脫那些好人，但只是說，“哦，是的”，并找到那些會刺激你的人。

例如，你不可能在不很快受到刺激的情況下與約翰·皮爾斯交談。我曾經和一群人交談過。例如，有埃德·吉爾伯特（Ed Gilbert）;我過去常常經常去他的辦公室，問他問題，聽他說話，回來后很興奮。我小心翼翼地挑選了我的員工，我和誰一起做過，或者我沒有集思廣益，因為吸音器是一種詛咒。他們只是好人;它們填滿了整個空間，除了吸收想法之外，它們什么也沒貢獻，新想法只是消失了，而不是回響。是的，我覺得有必要與人交談。我認為閉門造車的人無法做到這一點，因此他們無法讓自己的想法更加清晰，例如“你有沒有注意到這邊有什么東西？我從來不知道它——我可以過去看看。有人指路。在我訪問這里時，我已經找到了幾本書，我回家后必須閱讀。當我認為人們可以回答我并給我我不知道的線索時，我會與人們交談并提出問題。我出去看看！

問題：在分配閱讀和寫作時間以及實際進行研究時，您做了什么樣的權衡？

漢明：在我早期的時候，我相信你應該花至少和你在原始研究上一樣多的時間進行潤色和演示。現在至少有 50% 的時間必須用于演示。這是一個很大的數字。

問題：圖書館工作應該付出多少努力？

漢明：這取決于領域。我會這樣說。貝爾實驗室有一個人，一個非常非常聰明的人。他總是在圖書館里;他閱讀了一切。如果你想要參考資料，你就去找他，他給你各種各樣的參考資料。但是在形成這些理論的過程中，我形成了一個命題：從長遠來看，不會有以他的名字命名的效果。他現在從貝爾實驗室退休，是一名兼職教授。他非常有價值;我不是在質疑這一點。他寫了一些非常好的《物理評論》文章;但是沒有以他的名字命名的效果，因為他讀得太多了。如果你一直閱讀別人的所作所為，你就會像他們一樣思考。如果你想思考不同的想法，那就做很多有創造力的人所做的事情——把問題弄清楚，然后拒絕看任何答案，直到你仔細地思考問題，你會怎么做，你如何稍微改變問題，成為正確的問題。所以是的，你需要跟上。您需要跟上更多的步伐才能找出問題所在，而不是閱讀以找到解決方案。閱讀對于了解正在發生的事情以及可能的情況是必要的。但是，通過閱讀來獲得解決方案似乎并不是進行出色研究的方法。所以我給你兩個答案。你讀;但重要的不是數量，而是你閱讀的方式。

問題：你如何讓你的名字附在事物上？

漢明：通過做偉大的工作。我會告訴你漢明窗的。我給Tukey帶來了很多次困難，我接到他從普林斯頓打給我的電話。我知道他在寫功率譜，他問我是否介意他把某個窗口稱為“漢明窗”。我對他說：'來吧，約翰;你很清楚，我只做了一小部分工作，但你也做了很多。他說：“是的，漢明，但你貢獻了很多小事;你有權獲得一些榮譽。所以他稱它為漢明窗。現在，讓我繼續。我經常嘲笑約翰真正的偉大。我說過，真正的偉大是當你的名字像安培、瓦特和傅里葉一樣時——當它用小寫字母拼寫時。漢明窗就是這樣來的。

問題：迪克，你愿意評論一下演講、寫論文和寫書之間的相對有效性嗎？

漢明：在短期內，如果你想明天刺激某人，論文非常重要。如果你想長期獲得認可，在我看來，寫書更多的是貢獻，因為我們大多數人都需要定位。在這個知識幾乎無限的時代，我們需要方向來找到自己的道路。讓我告訴你什么是無限的知識。從牛頓時代到現在，我們的知識幾乎每 17 年翻一番，或多或少。我們基本上通過專業化來應對這個問題。按照這個速度，在未來的340年里，將有20個翻倍，即100萬個，現在每個領域將有100萬個專業領域。這不會發生。目前知識的增長將自我扼殺，直到我們獲得不同的工具。我相信，那些試圖消化、協調、擺脫重復、擺脫不那么富有成效的方法并清楚地呈現我們現在所知道的基本思想的書籍，將是后代將珍視的東西。公開演講是必要的;私下會談是必要的;書面論文是必要的。但我傾向于相信，從長遠來看，省略不重要的東西的書比告訴你一切的書更重要，因為你不想知道一切。我不想知道那么多關于企鵝的事情是通常的回答。你只想知道本質。

問題：你提到了諾貝爾獎的問題，以及隨后對一些職業的惡名。這難道不是一個更寬泛的名聲問題嗎？一個人能做什么？

漢明：您可以做的一些事情如下。大約每七年，在你的領域做出一次重大的（如果不是完全的）轉變。因此，我定期從數值分析轉向硬件，再到軟件等等，因為你往往會用盡你的想法。當你進入一個新的領域時，你必須像嬰兒一樣重新開始。你不再是大麂麝香，你可以從那里開始，你可以開始種植那些橡子，這些橡子將成為巨大的橡樹。我相信，香農毀了自己。事實上，當他離開貝爾實驗室時，我說，“香農的科學生涯就這樣結束了。我從朋友那里收到了很多抨擊，他們說香農一如既往地聰明。我說，'是的，他會同樣聰明，但這就是他科學生涯的終結，'我真的相信是這樣。

你必須改變。過了一會兒你就會累;你在一個領域用盡了你的獨創性。你需要在附近買點東西。我并不是說你從音樂轉向理論物理學再到英國文學;我的意思是，在你的領域內，你應該改變區域，這樣你就不會過時。你不能強迫每七年改變一次，但如果可以的話，我會要求你做一個研究的條件，就是你每七年改變一次你的研究領域，并合理地定義它意味著什么，或者在10年結束時，管理層有權強迫你改變。我會堅持改變，因為我是認真的。老家伙們發生的事情是，他們掌握了一種技術;他們繼續使用它。他們正朝著那個方向前進，當時是正確的，但世界變了。有新的方向;但老家伙們仍然朝著他們以前的方向前進。

你需要進入一個新的領域來獲得新的觀點，并且在你用完所有舊觀點之前。你可以為此做點什么，但這需要努力和精力。說：“是的，我會放棄我的名聲，這需要勇氣。例如，當糾錯碼被很好地推出時，有了這些理論，我說，“漢明，你要停止閱讀該領域的論文了;你將完全忽略它;你要試著做點別的事情，而不是在那上面滑行。我故意拒絕繼續從事這個領域。我甚至不會看報紙來強迫自己有機會做別的事情。我管理了自己，這就是我在整個演講中所宣講的。我知道我自己的許多缺點，所以我管理自己。我有很多缺點，所以我有很多問題，即管理的可能性很多。

問題：你會比較研究和管理嗎？

漢明：如果你想成為一名偉大的研究人員，你不會成為公司的總裁。如果你想成為公司的總裁，那是另一回事。我不反對擔任公司總裁。我只是不想。我認為伊恩·羅斯（Ian Ross）作為貝爾實驗室的總裁做得很好。我不反對;但你必須清楚你想要什么。此外，當你年輕的時候，你可能已經選擇了成為一名偉大的科學家，但隨著你壽命的延長，你可能會改變主意。例如，有一天我去找我的老板博德，問他：“你為什么會成為部門主管？你為什么不做一個好科學家呢？他說，“漢明，我對貝爾實驗室的數學應該是什么樣子有一個愿景。我看到如果這個愿景要實現，我必須實現它;我必須成為部門主管。當你對自己想做的事情的愿景是你可以單槍匹馬做的事情時，那么你應該追求它。有一天，你的愿景，你認為需要做的事情，比你單槍匹馬所能做的事情更大，那么你就必須轉向管理。愿景越大，你必須在管理上走得越遠。如果你對整個實驗室或整個貝爾系統應該是什么樣子有一個愿景，你必須到達那里才能實現它。你不能很容易地從底部實現它。這取決于你有什么目標和愿望。當他們在生活中發生變化時，你必須準備好改變。我選擇避免管理，因為我更喜歡單槍匹馬地做我能做的事情。但這是我做出的選擇，而且是有偏見的。每個人都有權選擇。保持開放的心態。但是，當你選擇一條道路時，看在天堂的份上，要意識到你做了什么，你做了什么，你做出了選擇。不要試圖兩面都做。

問題：一個人的期望有多重要，或者在一個團隊中或周圍被期望你做出出色工作的人有多重要？

漢明：在貝爾實驗室，每個人都希望我能做出好的工作——這對我有很大的幫助。每個人都希望你做得很好，所以如果你有自豪感，你就去做。我認為身邊有一流的人是非常有價值的。我尋找最優秀的人。物理桌失去最優秀的人的那一刻，我離開了。當我看到化學表也是如此的那一刻，我就離開了。我試著和那些能力很強的人一起去，這樣我就可以向他們學習，并期望我能取得好成績。通過刻意管理自己，我認為我比自由放任做得更好。

問題：在演講開始時，你最小化或淡化了運氣;但你似乎也掩蓋了把你帶到洛斯阿拉莫斯，把你帶到芝加哥，把你帶到貝爾實驗室的情況。

漢明：有一些運氣。另一方面，我不知道備用分支。除非你能說其他分支不會同樣或更成功，否則我不能說。你做的特別的事情是運氣嗎？例如，當我在洛斯阿拉莫斯見到費曼時，我知道他將獲得諾貝爾獎。我不知道為什么。但我很清楚他會做偉大的工作。無論將來出現什么方向，這個人都會做偉大的工作。果然，他確實做得很好。并不是說你在這種情況下只做了一點點偉大的工作，那是運氣，遲早有很多機會。有一大堆機會，如果你處于這種情況，你就會抓住一個機會，你在那邊而不是在這里很棒。有運氣的成分，是和否。運氣眷顧有準備的頭腦;運氣眷顧有準備的人。不能保證;我不保證成功是絕對確定的。我會說運氣會改變賠率，但個人有一些明確的控制。

那么，去吧，做偉大的工作！

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