Scientist: Four golden lessons

STEVEN WEINBERG

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.

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 over-simplified 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.

《Nature》上給青年科研工作者的幾條忠告

Steven Weinberg：四條黃金忠告

Steven Weinberg 現(xiàn)在得克薩斯大學物理系。本文以他 2003年6月在麥克基爾大學科學大會上的講話為基礎。

當我得到大學學位的時候 － 那是百八十年前的事了 －物理文獻在我眼里就象一個未經探索的汪洋大海，我必須在勘測了它的每一個部分之后才能開始自己的研究。做任何事情之前怎么能不先了解所有已經做過了的工作呢？萬幸的是，在我做研究生的第一年，我碰到了一些資深的物理學家，他們不顧我憂心忡忡的反對，堅持我應該開始進行研究，而在研究的過程中學習所需的東西。這可是生死悠關的事。我驚訝地發(fā)現(xiàn)他們的意見是可行的。我設法很快就拿到了一個博士學位 －雖然我拿到博士學位時對物理學還幾乎是一無所知。不過，我的確得到了一個很大的教益：沒有人了解所有的知識，你也不必。

另一個忠告就是，如果繼續(xù)用我的海洋學的比喻的話，當你在大海中搏擊而不是沉沒時，應該到波濤洶涌的地方去。19世紀60年代末，我在麻省理工大學教書時，一個學生找我說，他想去做廣義相對論領域的研究，而不愿意做我所在的領域－基本粒子物理學－方向的研究，原因是前者的原理已經很清楚，而后者在他看來則是一團亂麻。而在我看來這正是做相反決定的絕好理由。粒子物理學是一個還可以做創(chuàng)造性工作的領域。它在那個時候的確是亂麻一團，但是，從那時起，許多理論物理學家、試驗物理學家的工作把這團亂麻梳理出來，將所有的（嗯，幾乎所有的）知識納入一個叫做標準模型的美麗的理論之中。我的忠告是：到混亂的地方去，那里才是行動所在的地方。

我的第三個忠告可能是最難被接受的。這就是要原諒自己虛擲時光。要求學生們解決的問題都是教授們知道可以得到解決的問題（除非教授非常地殘酷）。而且，這些問題在科學上是否重要是無關緊要的，－必須解決他們以通過考試。但是在現(xiàn)實生活中，知道哪些問題重要是非常困難的，而且在歷史某一特定時刻你根本無從知道某個問題是否有解。二十世紀初，幾個重要的物理學家，包括 Lorentz 和 Abraham, 想創(chuàng)立一種電子理論。部分原因是為了理解為什么探測地球相對以太運動的所有嘗試都失敗了。我們現(xiàn)在知道，他們研究的問題不對。在當時，沒有人能夠創(chuàng)立一個成功的電子理論，因為量子力學尚未發(fā)現(xiàn)。需要到1905年，天才的愛因斯坦認識到正確的問題是運動在時間空間測量上的效應。沿著這條路線，他創(chuàng)立了相對論。因為你總也不能肯定哪個才是要研究的正確問題，你在實驗室里，在書桌前的大部分時間是會虛擲的。

如果你想要有創(chuàng)造性，你就必須習慣于大量時間不是創(chuàng)造性的，習慣于在科學知識的海洋上停滯不前。

最后，學一點科學史，起碼你所研究的學科的歷史。至少學習科學史可能在你自己的科學研究中有點用。比如，科學家會不時因相信從培根到庫恩、玻普這些哲學家所提出的過分簡化的科學模型而受到桎梏。科學史的知識是科學哲學的最好解毒劑。

更重要的是，科學史的知識可以使你覺得自己的工作更有意義。作為一個科學家，你很可能不會太富裕，你的朋友和親人可能也不理解你正在做的事情。而如果你研究的是象基本粒子物理學這樣的領域，你甚至沒有是在從事一種馬上就有用的工作所帶來的滿足。但是，認識到你進行的科學工作是歷史的一部分則可以給你帶來極大的滿足。

看看100年前，1903年。誰是1903年大英帝國的首相、誰是1903年美利堅合眾國的總統(tǒng)在現(xiàn)在看來有多重要呢？真正凸現(xiàn)出重要性的是 1903年Ernest Rutherford 和Frederick Soddy 在Mxxxxll 大學揭示了放射性的本質。這一工作（當然！）有實際的應用，但更加重要的是其文化含義。對放射性的理解使物理學家能夠解釋為什么幾百萬年以后太陽和地心仍是滾燙的。這樣，就清除了許多地質學家和古生物學家認為地球和太陽存在了很長年代的最后一個科學上的障礙。從此以后，基督教徒和猶太教徒就不得不或者放棄圣經的直接真理性或者放棄理性。這只是從加利略到牛頓、達爾文，直到現(xiàn)在削弱宗教教條主義桎梏的一系列步伐中的一步。只要讀讀今天的任何一張報紙，你都會知道這一工作還沒有完成。但是，這是一個文明化的工作，對這一工作科學家是可以感到驕傲的。