Scientist: Four golden lessons 


Nature 426, 389 (27 November 2003); doi:10.1038/426389a  

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.



Steven Weinberg 现在得克萨斯大学物理系。本文以他 2003年6月在麦克基尔大学科学大会上的讲话为基础。



  我的第三个忠告可能是最难被接受的。这就是要原谅自己虚掷时光。要求学生们解决的问题都是教授们知道可以得到解决的问题(除非教授非常地残酷)。而且,这些问题在科学上是否重要是无关紧要的,必须解决他们以通过考试。但是在现实生活中,知道哪些问题重要是非常困难的,而且在历史某一特定时刻你根本无从知道某个问题是否有解。二十世纪初,几个重要的物理学家,包括 Lorentz 和 Abraham, 想创立一种电子理论。部分原因是为了理解为什么探测地球相对以太运动的所有尝试都失败了。我们现在知道,他们研究的问题不对。在当时,没有人能够创立一个成功的电子理论,因为量子力学尚未发现。需要到1905年,天才的爱因斯坦认识到正确的问题是运动在时间空间测量上的效应。沿着这条路线,他创立了相对论。因为你总也不能肯定哪个才是要研究的正确问题,你在实验室里,在书桌前的大部分时间是会虚掷的。如果你想要有创制性,你就必须习惯于大量时间不是创造性的,习惯于在科学知识的海洋上停滞不前。   



  看看100年前,1903年。谁是1903年大英帝国的首相、谁是1903年美利坚合众国的总统在现在看来有多重要呢?真正凸现出重要性的是1903年Ernest Rutherford 和Frederick Soddy 在McGill 大学揭示了放射性的本质。这一工作(当然!)有实际的应用,但更加重要的是其文化含义。对放射性的理解使物理学家能够解释为什么几百万年以后太阳和地心仍是滚烫的。这样,就清除了许多地质学家和古生物学家认为地球和太阳存在了很长年代的最后一个科学上的障碍。从此以后,基督教徒和犹太教徒就不得不或者放弃圣经的直接真理性或者放弃理性。这只是从加利略到牛顿、达尔文,直到现在削弱宗教教条主义桎梏的一系列步伐中的一步。只要读读今天的任何一张报纸,你都会知道这一工作还没有完成。但是,这是一个文明化的工作,对这一工作科学家是可以感到骄傲的。