史蒂文·溫伯格（Steven Weinberg，1933年5月3日－），生於紐約，美國物理學家，1979年獲諾貝爾物理學獎。
《Four golden lessons》，是美國物理學家、諾貝爾獎(1979)獲得者Steven Weinberg發表在Nature-scientist 上的一篇文章，文章中，溫伯格為即將進入科研領域的研究生總結了四條箴言。
Advice to students at the start of their scientific careers。
文章英文原文深入淺出，行文優美。是科學大師溫伯格近50年科研生涯的感悟和總結。堪稱經典，讀後獲益匪淺，受到很多科研大牛及導師力薦。
顏寧（國際著名生物學家，美國國家科學院外籍院士）看到後，感嘆「寫的真好」！「竟然是第一次看到這篇11年前的短文」。
以下為《Four golden lessons》的中文譯文/英文原文：
golden lessons1:
沒人通曉一切，你也不必如此
No one knows everything, and you don't have to.
我取得學士學位的時候，距今已經很遙遠了。那時，物理學文獻對我來說，就是一片廣闊而未知的海洋。在開始任何研究之前，我都想仔細研究它每個部分的內容。因為，如果不知道這個領域的都已經做過的每個研究，我又如何能開展研究呢？幸運的是，讀研究生的第一年，我運氣很好。儘管我滿心焦慮，但卻得到了資深物理學者們的引導，他們堅持認為，我必須先開始研究，在研究過程中獲取相關的知識。這就好比遊泳，要麼選擇淹死，要麼奮力遊過去。令我驚訝的是，我發現這樣做真的有用，我很快便獲得了一個博士學位。儘管拿到博士學位時，我對物理學幾乎一無所知，但是我確實學到了一個重要道理：沒人通曉一切，你也不必如此。
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.
golden lessons2:
向混亂進軍，因為那裡才大有可為
Go for the messes - that's where the action is.
如果繼續用遊泳來打比方，我學到的另一個重要道理就是：遊泳時不想被淹死，就應該到湍急的水域去練習。上世紀60年代末，我在麻省理工學院教書時，一個學生告訴我，他想去研究廣義相對論，而不是我本人研究的專業粒子物理學。他的理由是，前者的原理已廣為人知，後者卻好似一團亂麻。在我看來，他所說的恰好是做出相反選擇的絕佳理由。粒子物理學還有許多創造性工作可以做，它在上世紀60年代確實像一團亂麻，但從那時起，許多理論和實驗物理學家逐漸釐清這團亂麻，把一切（幾乎一切）納入一個我們現在所說的一個叫做「標準模型」的理論。所以我的建議是：向混亂進軍，因為那裡才大有可為。
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.
golden lessons3:
原諒自己浪費時間
Forgive yourself for wasting time .
我的第三條建議或許最難被接受：那就是原諒自己浪費時間。學生們只被要求回答教授們（當然，不包括殘忍的教授）認為存在答案的問題。但是，這些問題是否具有重要的科學意義也無關緊要——因為解答這些問題的意義只為了讓學生通過考試。但在現實世界中，你很難知道這些問題是否重要，而且在歷史的某一時刻你甚至無法知道這個問題是否有解。二十世紀初，包括洛倫茲（Lorentz）和亞伯拉罕（Abraham）在內的幾位重要物理學家試圖建立一個電子理論，部分原因是為了解釋為何地球在以太中運動所產生的效應為何無法被探測到。我們現在知道了，他們在試圖解決一個錯誤的問題。當時，沒人能提出一個成功的電子理論，是因為那時還沒發現量子力學。直到1905年，天才的科學家阿爾伯特·愛因斯坦才發現，需要研究的問題應該是運動對時空測量的效應。從這一思路出發，他才創建了狹義相對論。你永遠也無法確定研究什麼樣的問題是正確的，所以你花在實驗室或書桌前的大部分時間都會被浪費掉。如果你想變得富於創造性，那你就應該習慣自己的大部分時間都沒有創造性，同樣應該習慣在迷路在科學知識的海洋裡。
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.
golden lessons4:
學習科學發展史，至少你研究的領域要了解
Learn something about the history of science,
or at a minimum the history of your own branch of science.
最後的建議是：學習科學發展史，至少，你研究領域的歷史要了解。最起碼，歷史可能為你自己的科研工作提供一定幫助。比如，過去和現在的科學家們常常會因為相信像培根（Francis Bacon）、庫恩（Thomas Kuhn）、波普爾（Karl Popper）等古代哲學家們所提出的過分簡化的科學模型而被阻礙。而掙脫古代哲學家思想束縛的最好方式，就是了解科學發展史。
更重要的是，對科學史的了解可以讓你更加清楚自己工作的價值。作為一名科學工作者，你可能永遠也不會變得富有；你的親戚和朋友或許也永遠不會懂你在做什麼；更進一步，如果你在像高能粒子物理學這樣的領域工作，你甚至無法獲得做那種立竿見影的工作所帶來的滿足感。但是，如果你意識到你的工作是世界科學歷史的一部分，你就能獲得極大的滿足感。
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.
回望百年前的1903年，誰是英國首相，誰是美國總統都已經不重要了。我們看來真正具有重要意義的，是盧瑟福（Ernest Rutherford）和索迪（Frederick Soddy）在麥吉爾大學揭示出了放射性的本質。這項工作當然有實際應用，但更重要的卻是其中的內涵。對放射性的了解使得物理學家終於能夠解釋，為何歷經數百萬年後，太陽和地球的內核仍然熾熱。從前許多地質學家和古生物學家認為太陽和地球有著極為巨大的年齡，這就消除了科學上對此最後的異議。自此以後，基督徒和猶太教徒要麼不得不放棄相信《聖經》所記載的教義，要麼不得不承認自己與理性毫不相干。從伽利略到牛頓，再到達爾文，再到現在的科學家，他們的研究一次又一次地削弱了教條主義的禁錮，而盧瑟福和索迪的工作只是其中的一步。當今，只要隨便閱讀一份報紙，你就會知道這項任務還未完成。不過，這是一項令社會文明化的工作，科學家應該為此工作感到驕傲。
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.
Article Source: Nature 426, 389 (27 November 2003)
doi:10.1038/426389a
Scientist: Four golden lessons by Steven Weinberg