Scientist-Four-golden-lessons
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当我拿到本科学位时，也许是一百年前的事了。物理学的文献对我来说就像一片广袤无垠、未经探索的海洋。我想我必须先遍历这其中所有的部分，才能开始自己的研究。如果我不知道前人已经完成的一切，那么我怎么可能有所作为呢？幸运的是，在读研的第一年，我有幸遇到几位资深物理学家。他们让我不要对那片汪洋忧心忡忡，坚持要求我必须立即开始研究，并在过程中边做边学。要么沉沦，要么扬帆起航。令我惊讶的是，这方法确实有效。我想办法快速获得了博士学位——尽管拿到学位时，我对物理学几乎一无所知。但我确实明白了一个重要的道理：没有人通晓一切，而且你也不必如此。
继续用我刚才的比喻，另一个需要吸取的教训是：当你在游泳而没有沉没时，应该主动游向波涛汹涌的地方。20世纪60年代末，我在麻省理工学院任教时，有个学生告诉我，他想研究广义相对论而非我当时从事的基本粒子，因为前者的原理已广为人知，而后者在他看来是一团混乱。我突然意识到，他恰恰给出了一个完全相反的好理由。但在我看来粒子物理学仍是一个能做出创造性成果的领域。虽然在60年代时它实在混乱不堪，但自那时起，许多理论和实验物理学家的工作已经理清了头绪，并将一切（好吧，是几乎一切）整合成一个优美的理论——标准模型。我的建议是：投身于混沌的领域，那里才是真正的机遇所在。
第三条建议可能是最难接受的：原谅自己浪费时间。学生只需要解决那些教授们知道有答案的问题（除非教授特别苛刻）。而这些问题是否具有科学价值并不重要——它们只是为了通过课程必须解决的障碍。但在现实世界中，你很难判断哪些问题真正重要，你永远无法确定某个问题在特定历史时刻是否可解。20世纪初，包括Lorentz和Abraham在内的几位顶尖物理学家曾试图建立电子理论，部分原由是为了解释为何所有探测地球穿过以太运动的实验都失败了。我们现在知道，他们研究的是错误的问题。在当时没人能发展出成功的电子理论，因为量子力学尚未诞生。直到1905年，Albert Einstein的天才头脑意识到，我们正确的研究方向应该是研究运动对时空测量的影响，这催生了狭义相对论。既然你永远无法确定哪些才是正确的研究方向，那么在实验室或书桌前度过的大部分时间终将被浪费。如果你想保持创造力，就必须习惯待在科学海洋长时间停滞不前的状态中——创造力迸发的时刻终究只是少数。
最后，去了解一些科学史——至少是你所研究领域的历史。最简单的理由是，这些历史知识或许真能对你的科研工作有所助益。比如，科学家偶尔会被某些*过度简化的科学理论所束缚，从Francis Bacon到Thomas Kuhn、Karl Popper*，他们提出过各种版本的模型都在此列。而科学史知识正是科学哲学最好的解毒剂。
更重要的是，科学史能让你更真切地体会到自身工作的价值。身为科学家，你大概率不会大富大贵。亲友们可能永远搞不懂你在做什么。如果从事的是基本粒子物理这类领域，你甚至无法获得”研究具有即时实用性”的满足感。但当你意识到自己的工作正在书写历史时，便能获得巨大的满足感。
回望1903年——距今100年前，当年额度英国首相或美国总统是谁还重要吗？真正闪耀在历史长河中的，是麦吉尔大学的Ernest Rutherford和Frederick Soddy正在揭开放射性的奥秘。这项研究当然有实际应用价值，但更深远的是它的文化影响力：对放射性的理解让物理学家得以解释为何太阳和地核在数百万年后仍能保持高温，从而消除了地质学家和古生物学家关于地球与太阳年龄的最后科学障碍。此后，基督徒和犹太教徒要么必须放弃对《圣经》字面真理的信仰，要么只能接受自身在真理之中边缘化的事实。这仅仅是Galileo-Newton-Darwin直至当代的一系列文明进程中的一步，它却持续削弱着宗教教条主义的桎梏。如今随便翻开报纸都能证明，这项事业尚未完成。但正是这种推动文明进步的工作，才最值得科学家为之自豪。
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.