这里我们给大家推送的是Karl Barry Sharpless教授2008年11月在中国天津大学Honeywell Nobel Lecture上给过的一个异常而且极为精彩的演讲。报告的题目是：“How to find something new”（如何发现新事物），Barry一生做过很多重要的演讲，但这个演讲可以说是其中最特殊的一次！（不论形式还是内容）
他告诉过我，这里是他数十年科研工作中最精华的一次总结和自述，（可能前后花的时间比他获得诺奖的汇报还要长，还要认真！）但是这个汇报并不是关于化学，而是关于科研方法和他自己关于科研创新的思考。我个人和这个PPT也结下了不解之缘：2009年3月份，也就是Barry在进行完这次报告后几个月，我加入了Scripps研究所他的课题组， 没几天他就看穿了我的弱点/特点-于是他将PPT和原稿赠送给了我，这也是他给我的最重要的一份礼物。 这个报告看了不下数百次，结合老先生十多年的教诲，学习感悟至深。直到自己建立了课题组，更是觉得有必要将这个翻译传播。这里我们会结合Barry的PPT逐页忠实地翻译他的PPT和原讲稿：
第一页：
如何发现新事物
讲稿：
Thank you, I am greatly honored to be visiting Tianjin University as the Honeywell Nobel lecturer.
How wonderful to see all the distinguished citizens and members of the Tianjin University community; and how exciting to see so many eager young scientists and engineers—I am looking at the future of China!
I am often asked, 'How do you find new reactions? Where do you get your ideas?"
翻译：
谢谢各位，我很荣幸受邀以霍尼韦尔诺贝尔奖演讲者的身份访问天津大学。
我非常高兴在此见到天津大学的所有杰出成员，也非常激动在此见到这么多热情的年轻科学家和工程师—在你们身上我看到了中国的未来！
经常有人问我，“您如何找到新的反应？您是从哪里得到那些新的想法的？”
第二页：
科学家中有收藏家，分类者和强迫症患者。从性格上讲，他们之间许多是侦探，许多是探险家；有些是艺术家，有些则是工匠。
---彼得·梅达瓦爵士
因对免疫学所做的杰出贡献而获得1960年诺贝尔生理学或医学奖
讲稿：
I think a good scientist must be very enthusiastic and very curious. To be successful, as well, you must be very ambitious.
But there are many kinds of scientists.
Sir Peter Medawar, a Nobel Laureate in Medicine, said:
“Among scientists are collectors, classifiers, and compulsive tidiers-up; many are detectives by temperament and many are explorers; some are artists and others artisans.”
I’m basically an explorer. Even if exploration doesn’t come naturally to you, I believe scientists of every temperament can learn to explore. I'd like to help everyone here become more creative, more open to opportunity, and, perhaps, be able to experience the thrill of making a discovery.
翻译：
我认为一位优秀的科学家必须非常热情且充满好奇。同时，他若想成功，野心也必不可少。
然而，科学家的种类很多。
诺贝尔生理学或医学奖得主彼得·梅达瓦（Peter Medawar）爵士曾说：
“科学家中有收藏家，分类者和强迫症患者。从性格上讲，他们之间许多是侦探，许多是探险家；有些是艺术家，有些则是工匠。”
我基本上是一位探险家。即使探索未知的能力并不是与生俱来的，但我相信各种性格的科学家都可以学习去探索。我想帮助在座各位变得更有创造力，在科学发现过程中能有更多的机遇，并且也许能体会到科学发现带来的那种激动人心的感受。
第三页：
千里之行，始于足下。
---《道德经》
讲稿：As it says in the TAO TE CHING:
The journey of a thousand miles starts with a single step.
翻译：正如《道德经》所言：
千里之行，始于足下。
第四页：
如果你想发现新事物，千里之行的第一步就是要学会与不确定性共存，并学会接受失败如常，因为寻找未知事物的风险就像成为一名从不系安全绳的高空杂技演员一样大。
讲稿：
The very first of the thousand steps, if you want to find something new, is to learn to live with uncertainty, and to learn to accept failure as the norm, because looking for the unknown is like being a trapeze artist who never works with a safety net.
There's no guarantee when, or even if, you'll make discoveries; no way of predicting whether what you find is what you went looking for.
By definition, you can't reason your way to anything really new, so you must journey into the unknown.
翻译：
如果你想发现新的事物，千里之行的第一步就是要学会与不确定性共存，并学会接受失败如常，因为寻找未知事物的风险就像成为一名从不系安全绳的高空杂技演员一样大。
并不能保证何时，甚至是否一定有新发现，也没有任何可能预测你所找到的新事物是否就是你希望寻找的。
根据新事物的定义，在已知范围内推理出真正的新事物是不可能的，因此你必须踏上通往未知之路。
第五页：
若想成功，必须冒失败的风险。
---王安
美籍华人电子学先驱
讲稿：
I have a personality that's very comfortable with uncertainty. I actually stayed a couple of extra years at Stanford in graduate school (doing the research equivalent of three Ph.D. theses) because I loved having total freedom—just running reactions in the lab or doing research in the library, no paperwork, no responsibilities to teach courses or write research grants.
While my reactions were running, I loved chalk-talking chemistry at the blackboard with other chemists.
I have never worried about security, or what the future might bring.
翻译：
我的性格使我乐观拥抱不确定性。实际上，我在斯坦福大学研究生院毕业后额外做了几年（做相当于三个博士学位论文工作量的）研究，因为我热爱完全的自由—只需在实验室中开反应或在图书馆中进行研究，除此之外没有文书工作、授课或撰写研究基金的的职责。
在做化学反应的闲暇时，我喜欢与其他化学家在黑板上进行“粉笔交谈”。
我从不担心个人的安全感或未来将给我带来什么。
第六页：
不怕惨败，才能有伟大的成就。
---约翰·肯尼迪
美国前总统
讲稿：
My Ph.D. supervisor, E.E. van Tamelen, was one of the most creative chemists of his generation, and he thought about the big problems. Since these are also the hardest problems, working for vT contributed even more to my being comfortable with uncertainty.
When you're pushing into the unknown, there's no guarantee of success, and so-called failure is your constant companion.
翻译：
我的博士导师范塔梅伦（E.E. van Tamelen）是他这一代中最具创造力的化学家之一，他所想的都是化学中的重要问题，同时这些科学问题往往也是最困难的，因此和他共事更使我乐观拥抱不确定性。
当你踏入未知世界时，就无法保证一定能成功，所谓的失败才是永恒的伴侣。
第七页：
我已经得到了很多实验结果，我已经知道了几千种不会成功的想法！
---托马斯·爱迪生
美国发明家
如果我有上千个想法，而最终只有一个想法是好的，我就心满意足了。
---阿尔弗雷德·诺贝尔
（对！就是那个诺贝尔，你没想错：）
讲稿：
I was very lucky. Prof van Tamelen gave us all a lot of freedom--he didn’t lay down explicit directions about what to do in the lab.
This helped me develop independence and confidence and maturity.
When I was at the bench, most of my reactions didn't work---but I never regarded them as failures.
My ideas that didn’t work always generated lots more ideas about what to do next.
So 'failure' became a concept I practically eliminated from my mental vocabulary.
翻译：
我很幸运，范塔梅伦教授给了我们很大的自由—他并未就我实验室的工作制定明确的方向。（感同身受！）
这有助于我获得独立性，增强信心和成熟度。
当我在实验台上工作时，我的大多数反应都行不通，但我从来没有将它们视为失败。
我行不通的想法总会给我带来关于下一步尝试的更多想法。
因此，我的词典里没有“失败”这个概念。
第八页：
我们要做的最重要的工作就是教会新雇员如何明智地失败。我们必须训练他们一遍一遍地进行实验，不断尝试和失败，直到他知道什么方案是行得通的。
发明家并不是一个墨守成规、死守书本的人。他尝试上千次可能都失败了，但只要成功一次，他就上道了。
---查尔斯·凯特林
美国著名工程师、发明家
讲稿：
From 1920 to 1947, Charles Kettering was head of research at one of the world’s largest companies, the auto manufacturer General Motors, and I share his views completely.
“Failing intelligently’ is a wonderful concept. You all need to learn how to fail intelligently.
Kettering says an inventor ‘tries and fails maybe a thousand times.’ From my experience, it’s closer to ten thousand times.
I imagine for most of you, it’s a big surprise to learn that, where making new discoveries is concerned, failure is really the path to success!
翻译：
从1920年到1947年，查尔斯·凯特林（Charles Kettering）曾担任全球最大的公司之一—通用汽车的研发总裁（被誉为创新之父），我非常赞同他的观点。
“明智地失败”是一个很棒的概念。你们都需要学习如何明智地失败。
凯特林说，一位发明家“尝试后可能会失败上千次。”而根据我的经验，失败的数量更接近上万次。
对于新的发现来说，失败才是真正的通向成功之路，我认为对你们在坐的大多数人来说（因为Barry认为下面的观众群都是精英，都认为自己很成功，一直都很成功：），听到这个道理真是一个很大的意外！
第九页：
我的那些失败启发了我最重要的发现。
---汉弗莱·戴维爵士
笑气、钙、钠、矿工安全灯的发现者/发明者
讲稿：
You must not think of failures as wasted time.
My own experience is similar to that of SirHumphrey Davy:
“The most important of my discoveries have been suggested to me by my failures.”
翻译：
一定不能将失败视为浪费时间。
我亲身的经历和汉弗莱·戴维（Humphrey Davy）爵士的经历相近：
“我的失败启发了我最重要的发现”
第十页：
迎接SERENDIPITY（意外发现）的到来
讲稿：
It’s not a contradiction to say that failures become a success, not when you understand the special role SERENDIPITY plays in making new discoveries.
Serendipity is the accidental discovery of something fortunate, often when you are looking for something entirely different.
The search for something new can never be an arational process.
What is really new is unknowable—by definition, the unknown can not be described or predicted.
So serendipity is ubiquitous among scientific discoveries.
For example, Kepler's proof for elliptical planetary orbits grew from his attempts to measure the areas & volumes of wine casks.
Likewise, nearly all the most valuable chemical processes in use today have an element of serendipity in their history.
翻译：
当理解了SERENDIPITY（意外发现）在发现新事物中所起的特殊作用后，失败转变为成功则是不矛盾的。
Serendipity通常指的是在寻找完全不同的事物时的偶然幸运发现。
寻找新事物永远不可能是一个理性的过程。
真正的新事物是未知的—根据定义，未知事物不可能被描述或被预测。
因此，意外发现在科学发现中无处不在。
例如，开普勒对椭圆形行星轨道的证明源于他对酒桶的面积和体积进行测量的尝试。
同样地，几乎当今所有最有价值的化学过程的发现都有意外的因素。
第十一页：
讲稿：
In fact, the birth of the modern chemical industry was due entirely to serendipity.
In 1856, W H Perkins was an 18yr old student trying to synthesize quinine. The reaction failed, and, as is so common with failures in the lab, he ended up with a nasty, black solid residue in the bottom of his flask. While cleaning the flask, he found that the mess contained a purple-colored compound that was soluble in alcohol.
Perkins followed up on this curious and totally unexpected result, and he discovered that the compound could dye textile fibers. He patented the new dye and started his own dye works.
Through pure serendipity, Perkins had discovered the first aniline coal-tar dye. But it was by seizing the serendipitous opportunity that Perkins became the modern chemical industry founding father.
The list of serendipitous discoveries is almost endless:
Columbus stumbled upon America while looking for the East Indies; the accidental discovery of polypropylene transform petroleum into the world we live in.
Teflon, penicillin, chemotherapy, X-rays, the pap smear, vaccination, Newton's law of gravitation, safety glass, artificial sweeteners, Vulcanized rubber, the Big Bang theory of creation, Silly Putty, popsicles, Coca Cola, the discovery of DNA, even the telephone—they all came along when something else was being looked at or looked for.
Many common drugs were created to treat different ailments: a candidate for treating angina with a remarkable side effect found a higher calling as Viagra!
I'm sorry to say that 'serendipity' was voted to be one of the ten most difficult words in the English language to translate. I hope it translates well into Chinese because scientific discoveries almost always owe a big debt to serendipity.
翻译：
实际上，现代化学工业的诞生完全是出于意外的发现。
1856年，珀金（Perkins）还是一名18岁的学生，他正在试图合成奎宁。他的反应失败了，这在实验室中稀松平常，他最后在烧瓶底部得到了一块令人不悦的黑色固体残渣。在清洗烧瓶时，他发现该固体残渣中含有一种可溶于乙醇的紫色化合物。
珀金对这个奇怪而完全出乎意料的结果进行了跟踪，他发现该化合物可以用于给纺织纤维染色。他为新染料申请了专利，并创建了自己的染料工厂。
通过纯粹的意外发现，珀金发现了第一种苯胺煤焦油染料。但是，正是通过抓住这个意外发现的机会，珀金才成为现代化学工业的奠基人。
意外发现的例子几乎是无止境的：
哥伦布在寻找东印度群岛时偶然发现了美洲大陆。聚丙烯的偶然发现将石油带进了我们所生活的世界。
特氟龙、青霉素、化学疗法、X射线、巴氏涂片、疫苗接种、牛顿万有引力定律、安全玻璃、人造甜味剂、硫化橡胶、宇宙大爆炸理论、橡皮泥、冰棒、可口可乐、DNA的发现，甚至是电话—它们都是在人们寻找其他事物时偶然发现的。
许多常见的药物在创制初期的目的都是用来治疗不同的疾病：一种治疗心绞痛的候选药物由于其显著的副作用--被称为“伟哥”，而被人们更加熟知！
很遗憾的是，“serendipity”被选为英语翻译中最困难的十个单词之一。我希望它能被很好地译成中文，因为其几乎所有的科学发现都欠她（serendipity）一个巨大的人情。
第十二页：
在观察所及的领域内，
机会只青睐有准备的头脑。
---路易斯·巴斯德，1854
（神之巴斯德，如果这句名言没听过的话，他另外一句你们一定听说过：科学虽然没有国界，但学者却有自己的祖国。）
讲稿：
If you wish to make discoveries, you must actively open the door and invite serendipity to come in.
But there is one person who I think has described it best. In 1854, Louis Pasteur famously wrote:
“Where observation is concerned, good luck favors only the prepared mind.”
翻译：
如果你想有新发现，则必须积极主动地开门邀请serendipity进入。
我认为有一个人将这件事描述得最好。1854年，路易斯·巴斯德（Louis Pasteur）曾写下他的名言：
在观察所及的领域内，机会只青睐有准备的头脑。
第十三页：
幸运与勇者为友。
幸运不是偶然,而是辛劳；
幸运之神昂贵的微笑是靠辛劳赢得。
不知何时黎明会来，我打开了所有的门。
希望意味着时刻为尚未出生的事物做准备。
---艾米丽·狄金森
（女）美国著名诗人
讲稿：
Perhaps you know about the famous British novelist Jane Austen. She never left home, never married, never traveled, but her novels--Pride and Prejudice is most famous--reveal a profound understanding of human nature--she was a true genius.
Less well known is a reclusive young woman from Massachusetts named Emily Dickinson. She and Walt Whitman are considered the greatest American poets of the 19th Century.
Jane Austen’s genius was for understanding human nature; Emily Dickinson had a genius for understanding the nature of creativity and human discovery. No one else expresses what I personally feel as well as she.
These lines from her poems beautifully express the role serendipity plays in life, as well as in scientific discovery:
Fortune befriends the bold.
Luck is not chance, it's toil; fortune's expensive smile is earned.
Knowing not when the dawn will come, I open every door.
To hope means to be ready at every moment for that which is not yet born.
翻译：
也许你知道英国著名小说家简·奥斯丁（Jane Austen）。她一生从未离家，从未结婚，也从未外出旅行，但她的小说《傲慢与偏见》却最为出名，其揭示了对人性的深刻理解，她是一个真正的天才。
鲜为人知的是一位来自马萨诸塞州的名叫艾米丽·狄金森（Emily Dickinson）的隐居年轻女士，她和沃尔特·惠特曼（Walt Whitman）被认为是19世纪最伟大的美国诗人。
简·奥斯丁的天才之处在于对人性的理解。艾米莉·狄金森的天才之处在于她可以理解人类创造力和发现的本质。我个人认为，在这方面，没人能比她描述得更加精妙。
她写的诗中的这些句子很好地表达了意外发现在生活以及科学中的作用：
幸运与勇者为友。
幸运不是偶然,而是辛劳；
幸运之神昂贵的微笑是靠辛劳赢得的。
不知何时黎明会来，我打开了所有的门。
希望意味着时刻为尚未出生的事物做好准备。
第十四页：
讲稿：
Call it serendipity, or good fortune, or chance, or luck.
But if you want to find something new, you follow it.
Discard your own plans in order to take advantage of good luck.
翻译：
称其为意外发现、好运、机会或运气吧。
如果你想发现新事物，请遵循它。
放弃你固执的计划，欢迎好运上门吧。
第十五页：
讲稿：Where’s the best place to look to make new discoveries?
翻译：哪里才是寻找新发现的最佳点？
第十六页：
你想在哪里寻找新发现？我的建议是：寻找新性质；研究过程
讲稿：
I sometimes say, if you want to get hit by a car, go stand in the middle of the freeway.
My lifelong method for ‘standing in the middle of the freeway’ started early.
Prof George Hammond from CalTech was a seminar speaker when I was a graduate student.
He was a real maverick, and what he said was heresy, because in those days the primary research targets of organic chemistry were synthesizing complex natural products, and making analogs of useful chemical compounds.
What Prof. Hammond said was:
“ Look for processes, not for products.”
翻译：
我有时会说，如果你想被汽车撞到，请站在高速公路的中间。
我毕生的“站在高速公路中间”的研究方法很早就开始使用了。
在我读研究生时，曾在研讨会上听过一次来自加州理工的乔治·哈蒙德（George Hammond）教授的演讲。
他是一个真正的特立独行者，他所说的内容在当时的被视为异端，因为在那时，有机化学的主要研究目标是合成复杂的天然产物及相关类似物。
哈蒙德教授那时说的是：
“ 关注过程，而不是产品。”
第十七页：
合成最根本和最持久的目标并不是合成新的化合物，而是合成新的功能。
---乔治·哈蒙德
加州理工教授
讲稿：
His message resonated in me—it was like an areligious conversion. What he said made perfect sense, despite it being practically the opposite of what was common practice in organic chemistry at the time.
I didn't think of it this way then, but I know now that I was violating a 'sacred cow.' I was deviating from accepted practice. I was freeing my mind.
He later wrote：
“The most fundamental and lasting objective of synthesis is not the production of new compounds, but the production of new properties.”
Production means processes. And if the chemistry is where you might want to find something new, process research is still, I believe, the best place to go.
And the old advice still holds true--find holes and fill them.
翻译：
他的话引发了我的共鸣，就像一场宗教转变。尽管实际上他的观点与当时有机化学的惯例相反，但他所说的却是非常合理的。
虽然现在我知道那时我在违背当年有机化学的“圣律”，但当时我并没有这样想。我偏离了公认的常识，并正在解放思想。
他后来写道：
“合成最根本和最持久的目标并不是合成新的化合物，而是合成新的功能。”
生产意味着过程。此外，若想在化学中找到新的东西，那么我相信研究过程仍然是最好的选择。
这条古老的建议至今仍然成立—找到过程之中漏洞并将它们填补。
第十八页：
第四步
治好你的“瘟疫”
Imagine that everyone has The Plague and that The Plague has a lot of different causes and symptoms.
Also, imagine that everyone is unaware of having any symptoms because it’s easy to live a normal life when you have The Plague.
Normal, in fact, means having The Plague!
Also, imagine that when someone recognizes plague symptoms, and he goes to the doctor and says, "I think I'm sick," all the doctors say, ” No, you’re normal, you're just fine.”
Here’s the problem:
Most doctors don’t know The Plague exists;
Some doctors have heard about The Plague, but don't believe in it because they weren’t taught about it in medical school;
A few doctors do know about The Plague, but their colleagues treat them like their nuts, and they can’t get published.
Why can’t they get published?
Because the very powerful doctors who run the medical journals and control government research funds are either disbelievers, or, what’s worse, they know about the Plague, but admitting that they know would be bad for their own business.
To me, The Plague is a metaphor for all the mental obstacles that stifle creativity and discovery, and scientific advances.
The biggest obstacle to creative thinking is all the baggage we carry around without realizing it.
想象每个人都患有“瘟疫”，而“瘟疫”有很多不同的病因和症状。
继续想象每个人都没有意识到他们有任何症状，因为人们即使在患“瘟疫”时也能继续过正常的生活。
实际上，“正常”意味着患有“瘟疫”！
还要想象一下，当有人发现其症状时，他对医生说：“我觉得我病了”，
而所有的医生都说：“不，你很正常，你没得病。”
这才是问题所在：
大多数医生都不知道“瘟疫”的存在；一些医生只是听说过“瘟疫”，但并不相信它真正存在，因为在医学院上课时，没人教过他们这类“瘟疫”。
一些医生确实了解“瘟疫”，但他们的同事们像对待疯子一样对待他们，因此这些医生的观点无法发表出来。
他们的观点为什么不能发表？
因为管理医学期刊和控制政府研究资金的那些非常有能力的医生要么不相信，要么，更糟的是，尽管他们知道“瘟疫”的存在，但承认他们所知道的会损害其利益。
对我而言，“瘟疫”是扼杀创造力、发现和科学进步的所有精神障碍的隐喻。
创造性思维的最大障碍是我们随身携带的所有没有被意识到的思维上的包袱。
第十九页：
你是多么容易被欺骗
讲稿：
We are all so very, very easy to fool.
Look at this picture.
Can you see all the little grey spots in the spaces between where the corners of the boxes intersect?
They may seem to move around. I can see them—can you? Raise your hand if you can see them!
Now focus on just one of those intersections; focus on a single grey spot.
Is it there?
No, of course not, because ALL those little grey spots are visual illusions. There's nothing in between the boxes.
You can have a lot of fun—just type 'VISUAL ILLUSIONS' into your web browser and you can see hundreds, probably thousands, of examples.
See how easy it is to be fooled? It's happening to you all the time. Visual illusions are physiological phenomena.
Our brains make unconscious assumptions for us, but they're not always right.
A lot of those assumptions are things you've learned. And many of them make your life a lot more difficult than it needs to be.
讲稿：
我们都非常，非常容易被欺骗。
大家请看这张图片。
你们能看到方格相交处的所有小灰点吗？
它们似乎四处移动。我可以看到它们—你们可以吗？如果你们可以看到，请举手！
现在只关注其中一个交点，专注于一个小灰点。
它还在吗？
不，当然不在，因为所有这些小灰点都是视觉错觉，方格之间并没有任何东西。
你们可以从中获得很多乐趣—只需在Web浏览器中输入“VISUAL ILLUSIONS（视觉错觉）”，就可以找到成百上千个例子。
看到被欺骗是多么容易了吗？这一直在你身上发生。视觉错觉是一种生理现象。
我们的大脑为我们做出了无意识的预设，但它们并非总是正确的。
这些预设中有很多是你们已经学到的，但也有很多使你们本来容易的生活变得更加困难。
（关于视觉欺骗和错觉，这里我补充一个Barry经常和我分享的极为有启发的视频。）
第二十页：
期望、傲慢、偏颇、恐惧、幻觉、妄想、神话、偏见、圣律、政治、资助、
非理性的忠诚
其中最糟糕的是：“亲情”—不理性地对你自己的想法照单全收
（Barry在这里用“亲情”点到的是科学家经常会犯的一个错误，也是科学研究方法的一个最关键问题，详见于“”）
讲稿：
I repeat: the biggest obstacle to creative thinking is all the baggage we carry around without realizing it.
What I called The Plague.
Expectations, pride, biases, phobias, illusions, delusions, myths, prejudices, sacred cows, politics, patronage, irrational loyalties (the worst of which is parental affection—irrationally loving your own ideas best)--I could go on and on.
These are the causes of the plague. If you want to be cured, you have to do it on your own--it’s not taught in the classroom.
Richard Feynman,the Nobel prize-winning physicist, and one of my greatest heroes said:
“The first principle is that you must not fool yourself - and you are the easiest person to fool.”
He also said:
“I'm smart enough to know I'm dumb.”
I urge you to read any of Feynman'sautobiographies and biographies. I think you'll see how Feynman's childhood, and especially his relationship with his father, gave him such a clear vision, a vision without the faults that most of us have.
When they went walking, his father would point out a bird and they would observe it, and his father would tell young Richard everything he knew about it. Feynman later wrote:
You can know the name of a bird in all the languages of the world, but when you're finished, you'll know absolutely nothing whatever about the bird... So let's look at the bird and see what it's doing -- that's what counts. I learned very early the difference between knowing the name of something and knowing something.
If you're a scientist, there are lots of false traps to fall in. The literature can be wrong. The definitions of where one discipline ends and another begin create mental barricades. Current fashions in research can be the result of funding trends or personality cults or even the biases of journal editors.
Here's something I wonder about: organic chemistry has had a single focus for well over fifty years, yet the most important reaction themes at our disposable were discovered before that time. What's the message? Is it possible that organic chemistry and women in 5" high heels are both fashion victims?
翻译：
我愿重申：创造性思维的最大障碍是我们随身携带的所有没有被意识到的思维上的包袱。
我称其为“瘟疫”。
期望、傲慢、偏颇、恐惧、幻觉、妄想、神话、偏见、圣律、政治、资助、非理性的忠诚（其中最糟糕的是父母的爱—最不理性地对你的想法照单全收）—我可以继续列举下去。
这些就是“瘟疫”的病因。如果你想痊愈，就必须靠自己—这不是在课堂上能教的。
理查德·费曼（Richard Feynman）是诺贝尔物理学奖得主，也是我最伟大的英雄之一，他曾说：
“首要原则是，切勿自欺欺人—而你自己是最容易被欺骗的人。”
他还说过：
“我很聪明，因为我知道我自己很傻。”
我强烈建议你们阅读费曼的自传和传记。我想你们会看到费曼的童年，尤其是他与父亲的关系如何赋予他如此清晰的洞见力，而不是像我们大多数人一样通过犯错而习得。
当他们散步时，他的父亲会指向一只鸟，二人一同观察。此外他的父亲会告诉年轻的理查德关于这只鸟他所知道的一切。费曼后来写道：
你可以用世界上所有的语言描述这只鸟的名字，但除此之外你还是对它几乎一无所知……所以让我们观察一下这只鸟在做什么—这才是有价值的。
我很早就学到了知道某物的名称和真正知道某物的区别。
如果你是一名科学家，就有可能落入有很多错误的陷阱。文献可能是错误的。一门学科衰败而另一门学科兴起带来了心理上的障碍。当前研究的“时尚”可能是基金驱动、个人崇拜甚至是期刊编辑偏见的结果。
这才是我想知道的事情：有机化学专注于一件事（复杂合成）已经50多年了，但那些我们日常使用中的最重要化学反应均在此之前就被发现了。这传递出什么信息？有机化学和穿着5英寸高跟鞋的女性是否都可能是“时尚”的受害者？
第二十一页：
自尊和他人的期望
不要在意别人所想
学会寻找尊敬、倾听、学习的对象
讲稿：
Not wanting other colleagues to think you’re dumb is probably the biggest impediment on Earth to thinking creatively.
It’s a kind of corollary of what I called Step 1, learning to live with uncertainty.
You can’t be creative if you can’t admit you’re wrong if you care too much about what others think of you.
You have to keep believing in yourself and your goals when you don’t have the full respect of your colleagues.
You must choose between what you want to do, and what others think you should do.
But if you want to be an explorer, you won’t be alone--there ARE others out there who want to follow the discovery path, and there ARE real role models who can support you and give you guidance.
My greatest role models, in addition to Prof van Tamelen, were Henry Taube, Jim Collman, and Bill Johnson at Stanford; Derek Barton at Imperial College, London; Gilbert Stork at Columbia, Albert Eschenmoser of the ETH (Swiss Federal Institute of Technology) in Zurich, and Saul Winstein at UCLA. I got to know them all when I was a young scientist, and I learned so much from my interactions with them.
Professors Taube and Barton later became Nobel Laureates, and I hope there may be yet more Nobelists on my list. These are scientists whose entire careers have been characterized by breadth of thinking and by discovery.
So to be an explorer, seek out good mentors and like-minded contemporaries, and learn to live without the support of the mainstream.
翻译：
不希望其他同事认为你很愚蠢，这可能是创造性思考的最大障碍。
这就是我所谓的“第一步”的必然结果，即学会如何与不确定性共存。
如果你不能承认自己错了，或者过分在意别人对你的看法，那么就无法发挥创造力。
即使当你缺乏同事的充分尊重时，也必须继续相信自己和你的目标。
你必须要在你自己想做什么和其他人认为你应该做什么之间进行选择。
但是，如果你想成为一名探险家，你将不会孤单—的确有人愿意遵循发现之路，也的确有真正的榜样可以为你提供支持和指导。
除了范塔梅伦教授，我最杰出的榜样是斯坦福大学的亨利·陶布（Henry Taube），吉姆·科尔曼（Jim Collman）和比尔·约翰逊（Bill Johnson）、帝国理工的德里克·巴顿（Derek Barton）、哥伦比亚大学的吉尔伯特·斯托克（Gilbert Stork）、瑞士联邦理工的阿尔伯特·埃申莫瑟（Albert Eschenmoser）和加州大学洛杉矶分校的索尔·温斯坦（Saul Winstein）。当我还是一个年轻的科学家时，我就认识了他们，从从与他们的交流中学到了很多。
陶布（Taube）和巴顿（Barton）教授后来都成为诺贝尔奖得主，我希望我的列表上还会有更多的诺贝尔奖得主。这些科学家的整个职业生涯都以思维广度和重要的科学发现为特征。
因此，要成为一名探索者，就需要寻找好的导师和志同道合的当代人，并学会在没有主流支持的情况下进行研究。
亨利·陶布（Henry Taube）（1915-2015）：美国无机化学家，因对金属配位化合物电子转移机理的研究获1983年诺贝尔化学奖。
吉姆·科尔曼（Jim Collman）（1932-）：美国无机生物化学家、有机生物化学家，揭示了呼吸和能量所必需的金属酶以及血液中氧运输所必需的血红蛋白和肌红蛋白的关键结构和功能细节。
德里克·巴顿（Derek Barton）（1918-1998）：英国化学家，因在研究有机化合物的晶体结构和络合物分子复杂的空间三维结构中对立体化学的发展作出巨大贡献获1969年诺贝尔化学奖。
吉尔伯特·斯托克（Gilbert Stork）（1921-2017）：美国有机合成化学家，研究方向为天然产物全合成，并发展了一系列以他命名的有机合成反应，如Stork烯胺化反应、Stork-Zhao烯基化反应等。
阿尔伯特·埃申莫瑟（Albert Eschenmoser）（1925-）：瑞士有机化学家，有机合成大师，以合成维生素B12成名。
索尔·温斯坦（Saul Winstein）（1912-1969）：加拿大物理有机化学家，碳正离子研究领域的代表人物，亲核取代反应中紧密离子对理论的提出者。
第二十二页：
复杂不是美德
国际象棋可能是娱乐活动中最深入，最耗费精力的项目，但仅此而已。对国际象棋天才而言，他也只是将大量的，难以被理解的智力天赋和努力集中在一个最终微不足道的人类事业上。
---乔治·史泰纳，1929—
一个真正的文艺复兴式的人物，
哥伦比亚大学，哈佛大学和牛津大学前教授
现就职于剑桥大学
讲稿：
One of the most difficult cults a scientist can join is complexity worship.
Doing scientific research that impresses because of its cerebral demands is not by itself a virtue: the question is, what has been accomplished that is of real value?
George Steiner says that a chess genius
“focuses vast, little-understood mental gifts and labors on an ultimately trivial human enterprise.”
I’m afraid a lot of our so-called leading scientists have vast mental gifts which they squander on
“ultimately trivial human enterprises.”
翻译：
科学家们最难以摆脱的狂热之一是复杂性崇拜。
进行因其研究方向的高智力需求而给人留下深刻印象的科学研究本身并不是一种美德：真正的问题是，已完成的哪些工作才具有真正的价值？
国际象棋天才乔治·斯坦纳曾说，
“将大量的，难以被理解的智力天赋和努力集中在一个最终微不足道的人类事业上。”
恐怕我们许多所谓的一流科学家都有超常的智力天赋，但他们把它浪费在“最终微不足道的人类事业”上。
第二十三页：
人—包括科学家在内，不理性地抗拒改变。
人们对“新事物”有非常开放的态度，只需要这些“新事物”与旧事物完全一样。
---查尔斯·凯特林
美国工程师、发明家
人脑对待一个新想法的方式就像身体对待一种陌生蛋白质一样：拒绝它。
---彼得·梅达瓦爵士
诺贝尔生理学或医学奖得主
讲稿：
PEOPLE—SCIENTISTS, TOO—IRRATIONALLY RESISTANCE.
We all resist change--it’s always easier to stay in the mainstream. It takes real effort to head off on your own.
The whole system fights change—funding agencies don’t want to finance speculation; groups of scientists create self-perpetuating empires.
As Sir Peter Medawar said：
“The human mind treats a new idea the way the body treats a strange protein: it rejects it.”
To be a discoverer, you must be able to change whenever circumstances change.
I used to drive my research group crazy because my circumstances changed so often!
If one group member had a very interesting result, within 24 hours I might have pulled everyone off their existing projects and sent them in a new direction. And when that research thread collapsed, because, of course, most do collapse, everyone might have their projects changed again within days, either following new opportunities that had been uncovered or returning to existing ideas.
I’m not saying this is a good way to run a research group--it’s not! But it is the fastest way to cover new scientific ground.
I succeeded because my group members have always been a hardy bunch. The best of them were like me, more excited about doing good science than the certainty of publications or a job.
Bless them all!
翻译：
人—包括科学家在内，不理性地抗拒改变。
我们都抗拒改变—始终跟随主流很容易。但掉头开创你自己与众不同的研究领域却需要付出真正的努力。
整个系统都在抗拒改变—资助机构不想资助风险大的研究；一群科学家创建了永存的科研帝国体系。
正如彼得·梅达瓦爵士所说：
“人脑对待一个新想法的方式就像身体对待一种陌生蛋白质一样：拒绝它。”
要成为发现者，我们必须能够在情况发生变化时改变计划。
我曾经使我的课题组陷入疯狂，因为我的研究情况经常改变！如果小组成员中做出一个非常有趣的结果，我可能会在24小时内让每个人都放下他们现有的课题，转入这一新的研究方向。当新的研究线索崩溃时，当然，因为大多数情况下这些线索确实崩溃了，每个人都可能会在几天内再次改变他们的课题，要么是继续研究已经发现的新机会，要么是回到之前的课题。
我并不是说这是管理课题组的好方法—并不是！但这是覆盖新科学领域的最快方法。
我之所以能够成功，是因为我的团队成员历来都是顽强的。他们中最优秀的人就像我一样，对出色的科学本身感到兴奋，这种追求胜过发表文章或找工作的确定性。
祝福他们！
第二十四页：
有些著名的科学家也不总是正确的，我们很多“已知”事实上是错误的。
我无法给任何年龄阶段的科学家们提供比这更好的建议：
关于一个假设成立的信念的强烈程度与该假设事实上是否真的成立毫无关系。
---彼得·梅达瓦爵士
诺贝尔生理学或医学奖得主
如果我们所有人的工作都基于这个假设：即那些被接受为“真”的理论就是真的，那么人类就没有什么进步的希望了。
---奥维尔·莱特
飞机的共同发明人
讲稿：
Sir Peter hits the nail on the head again:
“I can not give a scientist of any age better advice than this: the intensity of a conviction that a hypothesis is true has no bearing over whether it is true or not.”
How do you combat the illusion that what we ‘know’ is right? If you’re a chemist, it means you must take the time to run the reactions all the way back to the origins of the chain of assumptions you are making.
It’s tedious but necessary.
I’m only aware of having made a real error in the literature once. It was due to a structural mistake. My co-workers and I accepted the absolute configuration of a structure that appeared in the literature. It was wrong, and we should have checked it.
Subsequent work in our lab discovered the error and we immediately published a retraction.
I see structural errors all the time. I rarely see retractions.
As a scientist, if you ever see ANYTHING questionable in your results, you must trace your assumptions all the way back to their origins by repeating the work in your own lab.
It's tedious. It’s working at the bottom of the pyramid. But it’s required of a good scientist.
I personally know someone whose career was destroyed by believing something in the literature that was wrong. It destroyed the veracity of his research and made him unemployable at the level someone of his brilliance deserved.
翻译：
彼得爵士再次一语中的：
“我无法给任何年龄的科学家提供比这更好的建议：关于一个假设成立的信念的强烈程度与该假设事实上是否真的成立成立毫无关系。”
如何应对我们认为我们所“知道的”是正确的这一错觉？如果你是化学家，则意味着你必须花时间将反应一直追溯到所做的假设链的起源。
这很枯燥，但有必要。
我知道我曾经在发表的文章中仅犯过一次真正的错误，这是由于结构上的错误所致。我和我的同事们接受了文献中某结构的绝对构型。但它是错的，我们本应该检查一下。
在实验室中的后续工作中发现了该错误后，我们立即发布了撤稿声明。
我经常看到结构的错误，但我很少看到有人撤稿。
作为科学家，如果你发现结果中有任何可疑之处，则必须通过重复实验，将假设一直追溯到其起源。
这很枯燥，就像在金字塔的底部工作一样。但是，这是成为一位优秀的科学家所必需的素质。
我认识一人，因为相信文献中的某些错误而毁了他的事业。这破坏了他研究的准确性，并使他失去了其天赋配得上的职务。
第二十五页：
了解极限
不可能以不被误解的某种方式表达观点。
我们的知识只可能是有限的，而我们的无知一定是无限的。
---卡尔·波普尔
科学哲学家
讲稿：
KNOW THE LIMITS ：
You must assume you will be misunderstood.
My way of dealing with that is not publishing a discovery immediately, but waiting to publish after real robustness has been demonstrated. Then I can provide a whole cookbook of examples of how to run my reactions. I try to cover all the obvious potential applications. I try to find and publish, the limits of a reaction's utility.
And yet, time and time again, I will see papers that complain about not getting the expected results from my reactions. I know my papers provided the correct information in the first place, and just proper reading of them would prevent poor results and wasted man-hours, but, as Karl Popper said:
“It is impossible to speak in such a way that you cannot be misunderstood.”
Too much is published, and too little of value is said. Much of what is published in the literature is simply not useful. Too few scientists pursue a discovery until they know it is genuinely robust.
In chemistry today, most authors don't even acknowledge, let alone compare, their claims with all similar claims that already exist in the literature.
This is either self-deception on a grand scale or unethical self-promotion.
翻译：
了解极限
必须假定自己会被误解。
我解决该问题的方法不是将所发现的成果立即发表，而是在证明了该反应真正的可靠之处后再等待发表。之后，我可以提供一个完整的指南以说明如何进行反应。我尝试将反应覆盖至所有明显的潜在应用。我试图找到该反应效用的极限所在并将其发表出来。
然而，一次又一次，我会看到一些文章抱怨我的反应没有得到预期的结果。我知道我的文章一开始就提供了正确的信息，若正确阅读可防止糟糕的结果和时间的浪费。然而，正如卡尔·波普尔（Karl Popper）所说：
“不可能以不被误解的某种方式表达观点。”
发表的文章过多，但实际价值却提得太少，以至于发表的文章中许多内容根本没用。在发现反应真正可靠之前，很少有科学家会将发现视为追求。
在当今的化学领域，大多数作者甚至都不承认他们的主张与已发表文献中的主张类似，更不用说进行比较了。
这要么是自欺欺人，要么是不那么道德的自我推销。
第二十六页：
知道何时停止
你错过的并不重要，重要的是你所找到的
在某些事业中，谨慎的无序才是真正的方法。
---赫尔曼·麦尔维尔
经典美国小说《白鲸》作者
讲稿：
KNOW WHEN TO STOP：
You need to know when what you miss doesn’t matter.
You need to remember: the only thing that is important is what you FIND.
In the discovery process, speed is everything. Remember, thousands of things won't work before you find something important.
It really upsets me to see time being lost when a member of my research group doesn't know when to stop.
Two things are very hard for tidy-minded people to learn:
First of all, MOVE on as soon as you know what's GOING on--dotting all the 'I's and crossing all the ‘T’s’ – is simply unnecessary.
Second, stop when your patient is dead. Dispose of the body and don’t bother with an autopsy. Resurrection later is always possible.
There's just so very, very much out there to discover, and so little time to do it.
I agree with HERMAN MELVILLE, the author of the great American 19th Century novel Moby Dick:
“There are some enterprises in which careful disorderliness is the true method.”
‘Careful disorderliness.’ Isn’t that a great concept!
翻译：
知道何时停止。
需要知道的是，从何时开始，你错过的将不再重要。
需要记住的是，唯一重要的事就是你发现的。
在发现的过程中，速度就是一切。请记住，在找到重要的结果之前，会有成千上万次的失败。
当我的组员不知道何时停止时，看到他们把时间浪费了真的令我很沮丧。
思维定势的人很难学习两件事：
首先，只要知道发生了什么就立即继续前进—过分关注没有意义的细节耗时费力而且是完全没有必要。
其次，当你的“病人”（研究对象，假设等）死亡时停止。处理掉“尸体”，不要费心解剖尸体。以后总有机会复活。
其实可以发现的东西非常非常多，只是我们的时间不够用。
我同意美国19世纪伟大小说《白鲸》的作者赫尔曼·麦尔维尔（HERMAN MELVILLE）在书中所写：
“在某些事业中，谨慎的无序才是真正的方法。”
“谨慎的无序”难道不是一个好主意吗？
第二十七页：
科学研究的方法并不科学，因此不要证明，而要证伪。
关注所有看似真的句子然后质疑它们。
---戴维·里斯曼
哈佛大学社会学家
科学中的真理可以定义为能够为通往下一个更好的理论开辟通道的最适合假说。对于科学家来说，每天早餐前放弃自己喜欢的假设是一项很好的锻炼，这使他们的思想保持年轻。
---康拉德·洛伦茨
因对个体和社会行为的构成和激发方面做所做贡而献获得
1973年诺贝尔生理学或医学奖
讲稿：
THE SCIENTIFIC METHOD ISN'T SCIENTIFIC—SO DON'T PROVE—DISPROVE
The most obvious case of something you’ve been taught that you need to forget is the so-called Scientific Method. the scientific Method says to propose a hypothesis and then prove it.
In fact, a good scientist should always have multiple working hypotheses in mind, and the object is to disprove them.
Whenever I have good results in the lab, I assume that something's wrong. Remember what Alfred Nobel said?
“If I have a thousand ideas and only one turns out to be good, I am satisfied. “
In fact, the more exciting your results are, the higher the probability that they’re wrong.
Henry Taube, the Stanford mentor I told you about, would sit in the front row at departmental seminars. I often remember him saying to the day's speaker something like:
"This worries me. It sounds too good to be true--Nature’s just not that slick."
Try to kill good results; try to knock them to pieces. Disprove all you can before moving on. David Riesman said:
“ Look at all the sentences which seem true and question them.”
KONRAD LORENZ said:
“Truth in science can be defined as the working hypothesis best suited to open the way to the next better one. It is a good morning exercise for a research scientist to discard a pet hypothesis every day before breakfast. It keeps him young."
翻译：
科学研究的方法并不科学，因此不要证明，而是证伪。
你曾经学过的但需要忘记的最明显例子是所谓的“科学方法”。科学的方法是提出一个假设，然后证明它。
实际上，优秀的科学家应该始终在脑海中有多个可行的平行假设，其目的是证伪它们。
每当我在实验室中取得好结果时，我就下意识的认为哪里出了问题。还记得阿尔弗雷德·诺贝尔（Alfred Nobel）所说的话吗？
“如果我有上千个想法，而最终只有一个想法是好的，我就心满意足了。”
实际上，试验的结果越令人兴奋，它们出错的可能性就越高。
我之前提过的斯坦福导师亨利·陶比（Henry Taube）在开研讨会时总会坐在前排，我记得他经常对当天的演讲者说：
“这让我感到担心，结果太好了倒不像是真的—大自然并没有那么精明。”
尝试扼杀好的结果，尝试把它们弄成碎片。在推进至下一步之前，请尽可能去证伪。
戴维·里斯曼（David Riesman）曾说：
“关注那些所有看似真实的句子并质疑它们。”
康拉德·洛伦茨（KONRAD LORENZ）曾说：
科学中的真理可以定义为能够为通往下一个更好的理论开辟通道的最适合假说。对于科学家来说，每天早餐前放弃自己喜欢的假设是一项很好的锻炼，这使他们的思想保持年轻。
第二十八页：
好的实验会扼杀有缺陷的理论；但我们的思想仍然活跃，可以再次猜测。
每当一个理论在你看来是唯一可能的解释的时候，就把它当作一个征兆：说明你既不理解该理论，也没有理解你打算解决的问题。
---卡尔·波普尔
科学哲学家
讲稿：
As usual, the great Karl Popper expressed it beautifully:
“ Good tests kill ...