BlueRed

原文地址：http://phoenixhou.spaces.live.com/blog/cns!90216AC81E219101!537.entry

这是2003年一期Nature上的文章，物理学家Steven Weinberg的演讲稿，读完之后感觉深得我心，随手译了一下放在这里，与同仁们共勉。

Steven Weinberg建立了弱电统一理论（即统一四种基本力中的弱相互作用和电磁力），对于他所提到的Standard Model的建立起了决定性的贡献。有人对于Standard Model的评价是"被确认得如此之好，好得无聊"（"the Standard Model is studied and confirmed so well that things are, almost boring"）。由于知识所限，有关于Standard Model的东西就去看他发在European Physics Journal上的面向专业听众的讲稿The Making of Standard Model吧。（European Physics Journal C. 34:5-13. 2004）

四条黄金的经验

Steven Weinberg

当我获得我的大学学位时--得有100年了吧--物理学文献在我看来犹如一片浩瀚无际未经探索的海洋，而我在开始自己的研究之前必须勘测完每一片海域。在我还没有了解别人所完成的一切之前我又怎么能做研究呢？幸运的是，我在研究生院的第一年当一位资深物理学家的小弟，而他在我焦虑的反对下依然坚持我必须先开始研究工作，然后再一步步了解我所必须学习的东西。要么被淹死，要么学会游泳。令我吃惊的是：这很管用。我很快拿到了博士学位--尽管我拿到学位时仍对物理学几乎一无所知。但我确实学到了一件重要的事：没人知道一切，你也无需如此。

我学到的第二条经验--继续使用关于海洋的比喻--当你没淹死而学会游泳之后，你应当总是瞄准危险水域。60年代后期我在麻省理工任教时，一名学生告诉我他想进入广义相对论而非我正在从事的基本粒子物理领域工作，因为前者的基本原理已经清楚了，而后者在他看来还是一团糟。这令我惊讶：他正好给出了一个做出相反选择的完美理由。那时粒子物理是一片依然能够进行创造性工作的领域。在60年代粒子物理确实是一团糟，但之后许多理论与实验物理学家的工作使得所有问题（呃，几乎所有）统一于一个美妙的理论之下，那就是标准模型理论。我的建议是：挑战混沌--那最刺激。

我的第三条建议恐怕是最难接受的，那就是原谅自己浪费时间。教授（除非异常地残忍）只会要求自己的学生去解决他知道能够被解决的问题。另外，这些问题的科学意义是否重大无关紧要--要通过课程就必须解决这些问题。然而在现实世界里，我们很难知道那些问题是重要的，并且你没法知道在某个给定的历史时期，一个问题是否是可解决的。在20世纪初，数位物理学先驱，包括洛仑兹和Abraham曾试图建立电子理论。这一工作部分是为了弄清楚为何所有探测地球在以太中运动效应的尝试均告失败。现在我们知道他们是在研究错误的问题。在那个时候，没有人可以建立起成功的电子理论，因为量子力学尚未被发现。得益于1905年阿尔伯特·爱因斯坦的天才，所有人才意识到应当研究的问题是运动对时空度量的效应。这导致了狭义相对论的建立。因为你永远也不能确定那些事应当研究的"正确的问题"，你在实验室或是书桌上耗费的大多数时间会被浪费掉。如果你想做出创造性的工作，那么你就不得不习惯于在大多数的时间毫无创造性，习惯于平静面对科学知识的海洋。

最后一点，学一点科学史，或者最低限度你所从事分支的历史。这样做最不重要的理由是历史可能对你自己的工作有所帮助。比如，科学家们偶尔会被从弗朗西斯·培根到托马斯·库恩、卡尔·波普的哲学家们所提出的、过度简化的科学模型所妨碍。一些科学史的知识是对抗科学哲学的最佳解毒剂。

更为重要的是，科学史能够使你的工作对你显得更有价值。作为一个科学家，你很可能富裕无望；你的朋友和亲人很可能无法理解你究竟在干些什么；而且如果你做的是诸如基本粒子物理领域的工作的话，你还无法获得"正在做着马上就能有用的事"的满足感。但当你认识到你的工作是科学历史的一部分时，你会有巨大的成就感。

回首100年前的1903年，谁当英国首相或是美国总统现在看来有何重要？真正特别重要的事在McGill大学，埃涅斯特·卢瑟福和弗雷德里克·索迪正要揭示放射能的本质。这一工作有实际的应用（当然！），但更为重要的是其蕴含的文化意义。对放射能的理解使得物理学家能够解释太阳与地球的核心怎样维持数百万年的高热。由此许多地质学家与古生物学家对于地球与太阳年龄最后的科学异议也告解除。从此以后，基督教徒与犹太教徒要么不得不放弃对圣经字面真实的确信，要么承认这种确信与理性无关。这只是自伽利略到牛顿、达尔文至今一连串对宗教原教旨主义控制的打击中的一步。阅读一下最近的任何报纸都足以使你明白，这一工作仍未完成。但这是一件启蒙性的工作，科学家们能够为之自豪。


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

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 the 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.