温伯格的金玉四言——至开始科学生涯的学生(中英文对照).doc

Steven Weinberg: Four golden lessonsNATURE | 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 dont 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 thats 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 doesnt matter if the problems are scientifically important they have to be solved to pass the course. But in the real world, its 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 Earths 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, youre probably not going to get rich. Your friends and relatives probably wont understand what youre doing. And if you work in a field like elementary particle physics, you wont 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 Earths 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._ 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.温伯格的金玉四言至开始科学生涯的学生Steven Weinberg: Four golden lessons原文刊自2003年11月23日自然杂志（）史蒂文温伯格 著张旭 译 很久以前，当我得到学士学位时，物理学文献对我而言是一个广阔而未知的大海。若不探察大海的每一部分并悉心编制海图，我将无法展开我自己的任何研究。若不了解他人已经完成的工作，我怎样才能开展自己的工作呢？幸运的是，我在研究生院的第一年，有幸接触到一些资深物理学家。他们使我超越原有观念的束缚，坚持要求我必须开始进行研究，在前行中挖掘需要学习的内容。如此一来，沉浮全看自己。我惊讶地发现他们的建议竟然可行。我努力尽快获得博士学位虽然当我拿到学位时，对于物理学几乎一无所知。但是，我懂得了一个很重要的道理：没有人了解全部，你也不必强求。 接下来要了解的一个经验，将继续使用我关于海洋的隐喻当你畅游而没有沉没时，你应该去挑战汹涌的海水。当上个世纪六十年代末期，我执教于麻省理工学院时，一个学生告诉我，他准备进入广义相对论的研究领域，而不是进入我所正在从事的基本粒子领域。因为前者的基本原理如此清晰明了，而后者却对他而言却显得一片混乱。我猛然领悟到他恰恰已经给出做出相反选择的绝佳理由。当时，粒子物理是一个仍然存在创造性工作的领域。虽然在六十年代该领域的确一片混乱，但自从那时起，许多理论物理学家和实验物理学家已开始理出头绪，把许多实验事实（更进步说，几乎所有事实）纳入一个被称为“标准模型”的优美理论中。我的建议是：追寻混乱那才是行动之所在。 我的第三个建议可能最难以接受宽容地对待自己空耗的时间。学生仅仅被要求解决那些他们的教授认为是可以解决的问题（除非教授非常残酷）。另外，问题的科学意义并无关紧要为了通过课程，不得不解决这些问题。但是在真实世界中，很难知道哪些问题是重要的，而且你无从知晓在历史的既定时刻一个问题是否可以被解决。在二十世纪开始时，几位物理学领袖包括洛仑兹和麦克尔逊，尝试建立一套电子理论。部分目的是为解开无法探测到地球相对以太运动效应之谜。我们现在知道他们试图破解的问题本身就是错误的。在当时，没有人能够建立一套成功的电子理论，因为量子力学尚未被创立。到了1905年，天才的爱因斯坦认识到，运动的时空度量效应才是问题所在。据此，他创立了狭义相对论。当你无法确定什么是研究中真正的问题所在时，你在实验室或者书桌前的大部分时间将被无情消耗掉。如果你想具备创造性，那么你将不得不习惯于投入大把时间而无任何创造性，习惯于在科