溫伯格的金玉四言
——至開始科學生涯的學生
Steven Weinberg: Four golden lessons
原文刊自2003年11月23日《自然》雜志（<NATURE>）
史蒂文?溫伯格 著
張旭 譯
很久以前，當我得到學士學位時，物理學文獻對我而言是一個廣闊而未知的大海。若不探察大海的每一部分并悉心編制海圖，我將無法展開我自己的任何研究。若不了解他人已經完成的工作，我怎樣才能開展自己的工作呢？幸運的是，我在研究生院的第一年，有幸接觸到一些資深物理學家。他們使我超越原有觀念的束縛，堅持要求我必須開始進行研究，在前行中挖掘需要學習的內容。如此一來，沉浮全看自己。我驚訝地發現他們的建議竟然可行。我努力盡快獲得博士學位——雖然當我拿到學位時，對于物理學幾乎一無所知。但是，我懂得了一個很重要的道理：沒有人了解全部，你也不必強求。
接下來要了解的一個經驗，將繼續使用我關于海洋的隱喻——當你暢游而沒有沉沒時，你應該去挑戰洶涌的海水。當上個世紀六十年代末期，我執教于麻省理工學院時，一個學生告訴我，他準備進入廣義相對論的研究領域，而不是進入我所正在從事的基本粒子領域。因為前者的基本原理如此清晰明了，而后者卻對他而言卻顯得一片混亂。我猛然領悟到他恰恰已經給出做出相反選擇的絕佳理由。當時，粒子物理是一個仍然存在創造性工作的領域。雖然在六十年代該領域的確一片混亂，但自從那時起，許多理論物理學家和實驗物理學家已開始理出頭緒，把許多實驗事實（更進步說，幾乎所有事實）納入一個被稱為“標準模型”的優美理論中。我的建議是：追尋混亂——那才是行動之所在。
我的第三個建議可能最難以接受——寬容地對待自己空耗的時間。學生僅僅被要求解決那些他們的教授認為是可以解決的問題（除非教授非常殘酷）。另外，問題的科學意義并無關緊要——為了通過課程，不得不解決這些問題。但是在真實世界中，很難知道哪些問題是重要的，而且你無從知曉在歷史的既定時刻一個問題是否可以被解決。在二十世紀開始時，幾位物理學領袖包括洛侖茲和麥克爾遜，嘗試建立一套電子理論。部分目的是為解開無法探測到地球相對以太運動效應之謎。我們現在知道他們試圖破解的問題本身就是錯誤的。在當時，沒有人能夠建立一套成功的電子理論，因為量子力學尚未被創立。到了1905年，天才的愛因斯坦認識到，運動的時空度量效應才是問題所在。據此，他創立了狹義相對論。當你無法確定什么是研究中真正的問題所在時，你在實驗室或者書桌前的大部分時間將被無情消耗掉。如果你想具備創造性，那么你將不得不習慣于投入大把時間而無任何創造性，習慣于在科學知識的海洋里徘徊不前。
最后，了解一些科學史，至少你自己所在科學分支的歷史。如此建議的最基本原因是，科學史對你自己的科學工作有些實際的用處。例如，科學家們偶爾會因輕信那些從弗朗西絲?培根到托馬思?庫恩和卡爾?波普等哲學家們提出的過于簡單的科學模型而受桎梏。對付科學哲學最好的解藥莫過具備科學史知識。
更為重要的是，科學史可以使你覺得自己的工作看起來更有價值。作為一位科學家，你可能將不會富有。你的朋友和親戚可能無法理解你的工作。另外，如果你從事于類似基本粒子物理這樣的領域，你甚至不能體會到工作立刻有用的滿足感。但是，通過認識到自己的科學工作將是歷史的一部分，會使你獲得極大的滿足。
回首100年前，到1903年。在1903年，誰是大英帝國首相，誰是合眾國總統，這個問題對現在而言能有多重要呢？真正有著重要意義的是，歐內斯特?盧瑟福和弗雷德里克?索迪揭示出放射性的本質！這個工作有著實際的應用（當然！），但是更重要的是它的文化含義。理解了放射現象，使得物理學家可以解釋太陽和地心如何在百萬年后仍舊保持高溫。這樣，最終解決對地球年齡問題的科學爭論。地質學家和古生物學家的認識是正確的，實際上地球和太陽的年齡非常之大。在此之后，基督教徒和猶太教徒要么不得不放棄對圣經中所謂的真理的信任，要么就置自身于非理性。這僅僅是從伽利略經由牛頓和達爾文到現在不斷地削弱宗教教條主義桎梏中的一步。只要閱讀當今的報紙，就足以讓你認識到這個工作還遠遠沒有結束。不過，這是一項創造人類文明的工作，科學家足以對此引以為豪。
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史蒂文?溫伯格現任教于美國德克薩斯大學奧斯汀分校物理學系。因創立基本粒子間弱相互作用和電磁相互作用統一理論，并預言了弱中性流的存在，溫伯格與格拉肖、薩拉姆共同獲得1979年諾貝爾物理學獎。
Steven Weinberg: Four golden lessons
NATURE | VOL 426 | 27 NOVEMBER 2003 |
When I received my undergraduate degree — about a hundred years ago — the physics literature seemed to me a vast, unexplored ocean, every part of which I had to chart before beginning any research of my own. How could I do anything without knowing everything that had already been done? Fortunately, in my first year of graduate school, I had the good luck to fall into the hands of senior physicists who insisted, over my anxious objections, that I must start doing research, and pick up what I needed to know as I went along. It was sink or swim. To my surprise, I found that this works. I managed to get a quick PhD — though when I got it I knew almost nothing about physics. But I did learn one big thing: that no one knows everything, and you don't have to.
Another lesson to be learned, to continue using my oceanographic metaphor, is that while you are swimming and not sinking you should aim for rough water. When I was teaching at the Massachusetts Institute of Technology in the late 1960s, a student told me that he wanted to go into general relativity rather than the area I was working on, elementary particle physics, because the principles of the former were well known, while the latter seemed like a mess to him. It struck me that he had just given a perfectly good reason for doing the opposite. Particle physics was an area where creative work could still be done. It really was a mess in the 1960s, but since that time the work of many theoretical and experimental physicists has been able to sort it out, and put everything (well, almost everything) together in a beautiful theory known as the standard model. My advice is to go for the messes — that's where the action is.
My third piece of advice is probably the hardest to take. It is to forgive yourself for wasting time. Students are only asked to solve problems that their professors (unless unusually cruel) know to be solvable. In addition, it doesn't matter if the problems are scientifically important — they have to be solved to pass the course. But in the real world, it's very hard to know which problems are important, and you never know whether at a given moment in history a problem is solvable. At the beginning of the twentieth century, several leading physicists, including Lorentz and Abraham, were trying to work out a theory of the electron. This was partly in order to understand why all attempts to detect effects of Earth's motion through the ether had failed. We now know that they were working on the wrong problem. At that time, no one could have developed a successful theory of the electron, because quantum mechanics had not yet been discovered. It took the genius of Albert Einstein in 1905 to realize that the right problem on which to work was the effect of motion on measurements of space and time. This led him to the special theory of relativity. As you will never be sure which are the right problems to work on, most of the time that you spend in the laboratory or at your desk will be wasted. If you want to be creative, then you will have to get used to spending most of your time not being creative, to being becalmed on the ocean of scientific knowledge.
Finally, learn something about the history of science, or at a minimum the history of your own branch of science. The least important reason for this is that the history may actually be of some use to you in your own scientific work.For instance, now and then scientists are hampered by believing one of the oversimplified models of science that have been proposed by philosophers from Francis Bacon to Thomas Kuhn and Karl Popper. The best antidote to the philosophy of science is a knowledge of the history of science.
More importantly, the history of science can make your work seem more worthwhile to you. As a scientist, you're probably not going to get rich. Your friends and relatives probably won't understand what you're doing. And if you work in a field like elementary particle physics, you won't even have the satisfaction of doing something that is immediately useful. But you can get great satisfaction by recognizing that your work in science is a part of history.
Look back 100 years, to 1903. How important is it now who was Prime Minister of Great Britain in 1903, or President of the United States? What stands out as really important is that at McGill University, Ernest Rutherford and Frederick Soddy were working out the nature of radioactivity. This work (of course!) had practical applications, but much more important were its cultural implications. The understanding of radioactivity allowed physicists to explain how the Sun and Earth's cores could still be hot after millions of years. In this way, it removed the last scientific objection to what many geologists and paleontologists thought was the great age of the Earth and the Sun. After this, Christians and Jews either had to give up belief in the literal truth of the Bible or resign themselves to intellectual irrelevance. This was just one step in a sequence of steps from Galileo through Newton and Darwin to the present that, time after time, has weakened the hold of religious dogmatism. Reading any newspaper nowadays is enough to show you that this work is not yet complete. But it is civilizing work, of which scientists are able to feel proud.
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■ Steven Weinberg is in the Department of Physics, the University of Texas at Austin, Texas 78712, USA. This essay is based on a commencement talk given by the author at the Science Convocation at McGill University in June 2003.