How to Do Great Work

作者：保罗·格雷厄姆

原文链接

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If you collected lists of techniques for doing great work in a lot of different fields, what would the intersection look like? I decided to find out by making it.

如果你收集了许多不同领域做出卓越工作的技巧清单，它们的交集会是什么样子？我决定亲自探索一番。

Partly my goal was to create a guide that could be used by someone working in any field. But I was also curious about the shape of the intersection. And one thing this exercise shows is that it does have a definite shape; it’s not just a point labelled “work hard.”

我的部分目标是创造一份适用于任何领域工作者的指南。但我也对这个交集的形状感到好奇。这个练习表明，这个交集确实有一个明确的形状；它不仅仅是一个标着”努力工作”的点。

The following recipe assumes you’re very ambitious.

以下方法假设你非常有雄心壮志。

The first step is to decide what to work on. The work you choose needs to have three qualities: it has to be something you have a natural aptitude for, that you have a deep interest in, and that offers scope to do great work.

第一步是决定要从事什么工作。你选择的工作需要具备三个特质：它必须是你有天赋的领域，你对它有浓厚的兴趣，并且它能提供做出卓越工作的空间。

In practice you don’t have to worry much about the third criterion. Ambitious people are if anything already too conservative about it. So all you need to do is find something you have an aptitude for and great interest in.

实际上，你不必太担心第三个标准。如果说有什么的话，雄心勃勃的人在这方面已经过于保守了。所以你只需要找到你有天赋且极感兴趣的事情。

¹ sounds straightforward, but it’s often quite difficult. When you’re young you don’t know what you’re good at or what different kinds of work are like. Some kinds of work you end up doing may not even exist yet. So while some people know what they want to do at 14, most have to figure it out.

这听起来很简单，但实际上往往相当困难。年轻时，你不知道自己擅长什么，也不了解不同类型的工作是什么样的。你最终可能会从事的某些工作甚至可能还不存在。因此，虽然有些人在14岁就知道自己想做什么，但大多数人都需要慢慢摸索。

The way to figure out what to work on is by working. If you’re not sure what to work on, guess. But pick something and get going. You’ll probably guess wrong some of the time, but that’s fine. It’s good to know about multiple things; some of the biggest discoveries come from noticing connections between different fields.

找出要做什么工作的方法就是去工作。如果你不确定要做什么，那就猜一猜。但要选择一个方向并开始行动。你可能有时会猜错，但这没关系。了解多个领域是好事；一些最重大的发现来自于注意到不同领域之间的联系。

Develop a habit of working on your own projects. Don’t let “work” mean something other people tell you to do. If you do manage to do great work one day, it will probably be on a project of your own. It may be within some bigger project, but you’ll be driving your part of it.

养成做自己项目的习惯。不要让”工作”变成别人告诉你要做的事。如果你有朝一日真的做出了伟大的工作，很可能是在你自己的项目上。它可能是某个更大项目的一部分，但你会主导属于你的那部分。

What should your projects be? Whatever seems to you excitingly ambitious. As you grow older and your taste in projects evolves, exciting and important will converge. At 7 it may seem excitingly ambitious to build huge things out of Lego, then at 14 to teach yourself calculus, till at 21 you’re starting to explore unanswered questions in physics. But always preserve excitingness.

你的项目应该是什么？任何在你看来令人兴奋且雄心勃勃的事情。随着年龄的增长和项目品味的演变，令人兴奋和重要的事情会逐渐趋同。7岁时，用乐高积木搭建巨大的东西可能看起来令人兴奋且雄心勃勃；14岁时，自学微积分可能是这样；直到21岁，你开始探索物理学中未解答的问题。但始终要保持那份兴奋感。

There’s a kind of excited curiosity that’s both the engine and the rudder of great work. It will not only drive you, but if you let it have its way, will also show you what to work on.

有一种兴奋的好奇心，它既是伟大工作的引擎，也是方向舵。它不仅会驱动你，如果你顺其自然，它还会指引你该做什么。

What are you excessively curious about — curious to a degree that would bore most other people? That’s what you’re looking for.

你对什么有着过度的好奇心——好奇到会让大多数人感到厌烦的程度？这就是你要寻找的。

Once you’ve found something you’re excessively interested in, the next step is to learn enough about it to get you to one of the frontiers of knowledge. Knowledge expands fractally, and from a distance its edges look smooth, but once you learn enough to get close to one, they turn out to be full of gaps.

一旦你找到了自己极度感兴趣的事物，下一步就是学习足够的知识，使你达到知识的前沿。知识是以分形方式扩展的，从远处看，它的边缘看起来很平滑，但一旦你学到足够接近边缘的程度，你会发现它充满了空白。

The next step is to notice them. This takes some skill, because your brain wants to ignore such gaps in order to make a simpler model of the world. Many discoveries have come from asking questions about things that everyone else took for granted.

下一步是注意到这些空白。这需要一些技巧，因为你的大脑倾向于忽视这些空白，以构建一个更简单的世界模型。许多发现都来自于对他人认为理所当然的事物提出问题。

²If the answers seem strange, so much the better. Great work often has a tincture of strangeness. You see this from painting to math. It would be affected to try to manufacture it, but if it appears, embrace it.

如果答案看起来很奇怪，那就更好了。伟大的工作往往带有一丝奇特。从绘画到数学，你都能看到这一点。刻意制造这种奇特感会显得做作，但如果它自然出现，就要欣然接受。

Boldly chase outlier ideas, even if other people aren’t interested in them — in fact, especially if they aren’t. If you’re excited about some possibility that everyone else ignores, and you have enough expertise to say precisely what they’re all overlooking, that’s as good a bet as you’ll find.

大胆追求那些异常的想法，即使其他人对它们不感兴趣——事实上，尤其是当他们不感兴趣的时候。如果你对某种被所有人忽视的可能性感到兴奋，而且你有足够的专业知识能准确指出他们都忽视了什么，这就是你能找到的最好的赌注。

³ steps: choose a field, learn enough to get to the frontier, notice gaps, explore promising ones. This is how practically everyone who’s done great work has done it, from painters to physicists.

四个步骤：选择一个领域，学习足够的知识以达到前沿，注意到空白，探索有前途的空白。这实际上是每个做出伟大工作的人所采用的方法，从画家到物理学家都是如此。

Steps two and four will require hard work. It may not be possible to prove that you have to work hard to do great things, but the empirical evidence is on the scale of the evidence for mortality. That’s why it’s essential to work on something you’re deeply interested in. Interest will drive you to work harder than mere diligence ever could.

第二步和第四步需要付出艰苦的努力。虽然可能无法证明做伟大的事情一定需要努力工作，但经验证据的力度堪比生命必有终结的证据。这就是为什么从事你深感兴趣的事情如此重要。兴趣能驱使你比单纯的勤奋更加努力工作。

The three most powerful motives are curiosity, delight, and the desire to do something impressive. Sometimes they converge, and that combination is the most powerful of all.

最强大的三种动机是好奇心、愉悦感和做出令人印象深刻的事情的欲望。有时这三者会融合在一起，这种组合是最强大的。

The big prize is to discover a new fractal bud. You notice a crack in the surface of knowledge, pry it open, and there’s a whole world inside.

最大的奖励是发现一个新的分形萌芽。你注意到知识表面的一道裂缝，将其撬开，里面是一个全新的世界。

Let’s talk a little more about the complicated business of figuring out what to work on. The main reason it’s hard is that you can’t tell what most kinds of work are like except by doing them. Which means the four steps overlap: you may have to work at something for years before you know how much you like it or how good you are at it. And in the meantime you’re not doing, and thus not learning about, most other kinds of work. So in the worst case you choose late based on very incomplete information.

让我们再多谈谈确定工作方向这个复杂的问题。之所以困难，主要是因为你无法在亲身体验之前了解大多数工作的真实情况。这意味着四个步骤是重叠的：你可能需要在某个领域工作多年，才能知道自己有多喜欢它或者在这方面有多擅长。与此同时，你没有接触，也就无法了解其他大多数类型的工作。因此，在最坏的情况下，你会基于非常不完整的信息做出迟来的选择。

⁴ The nature of ambition exacerbates this problem. Ambition comes in two forms, one that precedes interest in the subject and one that grows out of it. Most people who do great work have a mix, and the more you have of the former, the harder it will be to decide what to do.

野心的本质加剧了这个问题。野心有两种形式，一种是先于对某个领域的兴趣而存在，另一种是从兴趣中成长起来的。大多数做出伟大工作的人都兼具这两种野心，而前一种野心越强，就越难决定该做什么。

The educational systems in most countries pretend it’s easy. They expect you to commit to a field long before you could know what it’s really like. And as a result an ambitious person on an optimal trajectory will often read to the system as an instance of breakage.

大多数国家的教育系统假装这很容易。他们期望你在真正了解一个领域之前就做出承诺。结果，一个走在最佳轨道上的雄心勃勃的人，在这个系统看来往往就是一个异常案例。

It would be better if they at least admitted it — if they admitted that the system not only can’t do much to help you figure out what to work on, but is designed on the assumption that you’ll somehow magically guess as a teenager. They don’t tell you, but I will: when it comes to figuring out what to work on, you’re on your own. Some people get lucky and do guess correctly, but the rest will find themselves scrambling diagonally across tracks laid down on the assumption that everyone does.

如果他们至少承认这一点就好了——承认这个系统不仅无法帮助你找出该做什么，而且是建立在假设你会在青少年时期神奇地猜对的基础上。他们不会告诉你，但我会：在确定该做什么这个问题上，你只能靠自己。有些人运气好，猜对了，但其他人会发现自己在为适应这个假设所有人都能猜对的系统而手忙脚乱。

What should you do if you’re young and ambitious but don’t know what to work on? What you should not do is drift along passively, assuming the problem will solve itself. You need to take action. But there is no systematic procedure you can follow. When you read biographies of people who’ve done great work, it’s remarkable how much luck is involved. They discover what to work on as a result of a chance meeting, or by reading a book they happen to pick up. So you need to make yourself a big target for luck, and the way to do that is to be curious. Try lots of things, meet lots of people, read lots of books, ask lots of questions.

如果你年轻有抱负，却不知道该做什么，该怎么办？你绝不应该消极地随波逐流，认为问题会自己解决。你需要采取行动。但没有一个系统的程序可以遵循。当你阅读那些做出伟大工作的人的传记时，你会惊讶地发现运气扮演了多么重要的角色。他们发现自己该做什么，往往是因为一次偶然的会面，或是随手拿起的一本书。所以你需要让自己成为幸运的大目标，而实现这一点的方法就是保持好奇心。尝试很多事情，结识很多人，阅读很多书，提出很多问题。

⁵ in doubt, optimize for interestingness. Fields change as you learn more about them. What mathematicians do, for example, is very different from what you do in high school math classes. So you need to give different types of work a chance to show you what they’re like. But a field should become increasingly interesting as you learn more about it. If it doesn’t, it’s probably not for you.

当有疑问时，优化有趣性。随着你对领域了解的加深，它们会发生变化。例如，数学家所做的工作与你在高中数学课上所做的大不相同。所以你需要给不同类型的工作一个机会，让它们向你展示它们的真实面貌。但是，一个领域应该随着你对它的了解而变得越来越有趣。如果不是这样，那它可能不适合你。

Don’t worry if you find you’re interested in different things than other people. The stranger your tastes in interestingness, the better. Strange tastes are often strong ones, and a strong taste for work means you’ll be productive. And you’re more likely to find new things if you’re looking where few have looked before.

如果你发现自己对与他人不同的事物感兴趣，不要担心。你在有趣性方面的品味越独特越好。独特的品味往往是强烈的，而对工作的强烈兴趣意味着你会富有成效。如果你在很少有人关注的地方寻找，你更有可能发现新事物。

One sign that you’re suited for some kind of work is when you like even the parts that other people find tedious or frightening.

一个迹象表明你适合某种工作，就是当你甚至喜欢其他人觉得乏味或可怕的部分时。

But fields aren’t people; you don’t owe them any loyalty. If in the course of working on one thing you discover another that’s more exciting, don’t be afraid to switch.

但领域不是人；你不欠它们忠诚。如果在从事一件事的过程中，你发现了另一件更令人兴奋的事，不要害怕转换。

If you’re making something for people, make sure it’s something they actually want. The best way to do this is to make something you yourself want. Write the story you want to read; build the tool you want to use. Since your friends probably have similar interests, this will also get you your initial audience.

如果你在为人们创造某些东西，确保那是他们真正想要的。做到这一点的最好方法是创造你自己想要的东西。写你想读的故事；构建你想使用的工具。由于你的朋友可能有相似的兴趣，这也会为你带来初始受众。

This should follow from the excitingness rule. Obviously the most exciting story to write will be the one you want to read. The reason I mention this case explicitly is that so many people get it wrong. Instead of making what they want, they try to make what some imaginary, more sophisticated audience wants. And once you go down that route, you’re lost.

这应该遵循兴奋感规则。显然，最令人兴奋的故事就是你想读的那个。我之所以明确提到这一点，是因为很多人在这方面犯错。他们不是创造自己想要的东西，而是试图创造一些想象中的、更高级的受众想要的东西。一旦你走上这条路，你就迷失了。

⁶ are a lot of forces that will lead you astray when you’re trying to figure out what to work on. Pretentiousness, fashion, fear, money, politics, other people’s wishes, eminent frauds. But if you stick to what you find genuinely interesting, you’ll be proof against all of them. If you’re interested, you’re not astray.

当你试图找出该做什么时，有很多力量会让你误入歧途。虚伪、时尚、恐惧、金钱、政治、他人的愿望、著名的骗局。但如果你坚持你真正感兴趣的东西，你就能抵御所有这些。如果你对某事感兴趣，你就不会偏离正轨。

Following your interests may sound like a rather passive strategy, but in practice it usually means following them past all sorts of obstacles. You usually have to risk rejection and failure. So it does take a good deal of boldness.

追随你的兴趣听起来可能是一种相当被动的策略，但在实践中，它通常意味着要克服各种障碍。你通常需要冒着被拒绝和失败的风险。所以这确实需要相当大的勇气。

But while you need boldness, you don’t usually need much planning. In most cases the recipe for doing great work is simply: work hard on excitingly ambitious projects, and something good will come of it. Instead of making a plan and then executing it, you just try to preserve certain invariants.

但是，虽然你需要勇气，但通常不需要太多计划。在大多数情况下，做出伟大工作的秘诀很简单：在令人兴奋的雄心勃勃的项目上努力工作，好的结果自然会随之而来。与其制定计划然后执行，不如试图保持某些不变量。

The trouble with planning is that it only works for achievements you can describe in advance. You can win a gold medal or get rich by deciding to as a child and then tenaciously pursuing that goal, but you can’t discover natural selection that way.

计划的问题在于，它只适用于你能提前描述的成就。你可以通过儿时的决定和之后的坚持不懈来赢得金牌或致富，但你无法用这种方式发现自然选择理论。

I think for most people who want to do great work, the right strategy is not to plan too much. At each stage do whatever seems most interesting and gives you the best options for the future. I call this approach “staying upwind.” This is how most people who’ve done great work seem to have done it.

我认为，对于大多数想做出伟大工作的人来说，正确的策略是不要过度计划。在每个阶段，做那些看起来最有趣且能为未来提供最佳选择的事情。我把这种方法称为”保持上风”。大多数做出伟大工作的人似乎都是这样做的。

Even when you’ve found something exciting to work on, working on it is not always straightforward. There will be times when some new idea makes you leap out of bed in the morning and get straight to work. But there will also be plenty of times when things aren’t like that.

即使你找到了令人兴奋的工作对象，从事这项工作也并不总是一帆风顺的。有时，一个新想法会让你一大早就跳下床直奔工作。但也有很多时候并非如此。

You don’t just put out your sail and get blown forward by inspiration. There are headwinds and currents and hidden shoals. So there’s a technique to working, just as there is to sailing.

你不能只是扬起帆，就被灵感吹向前方。有逆风、暗流和隐藏的浅滩。所以工作也有技巧，就像航海一样。

For example, while you must work hard, it’s possible to work too hard, and if you do that you’ll find you get diminishing returns: fatigue will make you stupid, and eventually even damage your health. The point at which work yields diminishing returns depends on the type. Some of the hardest types you might only be able to do for four or five hours a day.

例如，虽然你必须努力工作，但也可能工作过度，如果这样做，你会发现收益递减：疲劳会使你变得愚钝，最终甚至会损害你的健康。工作开始收益递减的点取决于工作类型。对于一些最困难的工作类型，你可能每天只能做四五个小时。

Ideally those hours will be contiguous. To the extent you can, try to arrange your life so you have big blocks of time to work in. You’ll shy away from hard tasks if you know you might be interrupted.

理想情况下，这些时间应该是连续的。尽可能安排你的生活，使你有大块的时间用于工作。如果你知道可能会被打断，你就会回避困难的任务。

It will probably be harder to start working than to keep working. You’ll often have to trick yourself to get over that initial threshold. Don’t worry about this; it’s the nature of work, not a flaw in your character. Work has a sort of activation energy, both per day and per project. And since this threshold is fake in the sense that it’s higher than the energy required to keep going, it’s ok to tell yourself a lie of corresponding magnitude to get over it.

开始工作可能比持续工作更困难。你经常需要欺骗自己来跨过那个初始门槛。不要为此担心；这是工作的本质，而不是你性格中的缺陷。工作有一种激活能，无论是每天还是每个项目都是如此。既然这个门槛是虚假的，因为它比保持工作所需的能量更高，所以告诉自己一个相应程度的谎言来跨过它是可以的。

It’s usually a mistake to lie to yourself if you want to do great work, but this is one of the rare cases where it isn’t. When I’m reluctant to start work in the morning, I often trick myself by saying “I’ll just read over what I’ve got so far.” Five minutes later I’ve found something that seems mistaken or incomplete, and I’m off.

如果你想做出伟大的工作，对自己撒谎通常是个错误，但这是少数例外之一。当我早上不愿开始工作时，我经常欺骗自己说”我只是看看到目前为止我做了什么”。五分钟后，我就会发现一些看起来错误或不完整的地方，然后我就开始工作了。

Similar techniques work for starting new projects. It’s ok to lie to yourself about how much work a project will entail, for example. Lots of great things began with someone saying “How hard could it be?”

类似的技巧也适用于开始新项目。例如，对自己撒谎，低估一个项目所需的工作量是可以的。许多伟大的事情都始于有人说”这能有多难？”

This is one case where the young have an advantage. They’re more optimistic, and even though one of the sources of their optimism is ignorance, in this case ignorance can sometimes beat knowledge.

这是年轻人有优势的一种情况。他们更乐观，尽管他们乐观的一个来源是无知，但在这种情况下，无知有时反而能战胜知识。

Try to finish what you start, though, even if it turns out to be more work than you expected. Finishing things is not just an exercise in tidiness or self-discipline. In many projects a lot of the best work happens in what was meant to be the final stage.

不过，要尽量完成你开始的事情，即使它最终比你预期的工作量更大。完成事情不仅仅是一种整洁或自律的练习。在许多项目中，最好的工作往往发生在本应是最后阶段的时候。

Another permissible lie is to exaggerate the importance of what you’re working on, at least in your own mind. If that helps you discover something new, it may turn out not to have been a lie after all.

另一个可以接受的谎言是夸大你正在做的事情的重要性，至少在你自己的心中是这样。如果这能帮助你发现新东西，那么它最终可能并不是一个谎言。

⁷ there are two senses of starting work — per day and per project — there are also two forms of procrastination. Per-project procrastination is far the more dangerous. You put off starting that ambitious project from year to year because the time isn’t quite right. When you’re procrastinating in units of years, you can get a lot not done.

由于开始工作有两种意义——每天和每个项目——所以也存在两种形式的拖延。按项目拖延远比按天拖延更危险。你一年又一年地推迟开始那个雄心勃勃的项目，因为时机似乎总是不够完美。当你以年为单位拖延时，你可能会有很多事情没有完成。

⁸ reason per-project procrastination is so dangerous is that it usually camouflages itself as work. You’re not just sitting around doing nothing; you’re working industriously on something else. So per-project procrastination doesn’t set off the alarms that per-day procrastination does. You’re too busy to notice it.

按项目拖延如此危险的一个原因是，它通常伪装成工作。你不是在无所事事；你在勤奋地做其他事情。所以按项目拖延不会像按天拖延那样触发警报。你太忙了，以至于没有注意到它。

The way to beat it is to stop occasionally and ask yourself: Am I working on what I most want to work on? When you’re young it’s ok if the answer is sometimes no, but this gets increasingly dangerous as you get older.

克服它的方法是偶尔停下来问自己：我正在做的是我最想做的事情吗？当你年轻时，答案有时是否定的也没关系，但随着年龄的增长，这变得越来越危险。

⁹ work usually entails spending what would seem to most people an unreasonable amount of time on a problem. You can’t think of this time as a cost, or it will seem too high. You have to find the work sufficiently engaging as it’s happening.

伟大的工作通常需要花费在大多数人看来不合理的时间来解决一个问题。你不能把这段时间看作是一种成本，否则它会显得太高。你必须在工作进行时就觉得它足够吸引人。

There may be some jobs where you have to work diligently for years at things you hate before you get to the good part, but this is not how great work happens. Great work happens by focusing consistently on something you’re genuinely interested in. When you pause to take stock, you’re surprised how far you’ve come.

可能有些工作需要你在多年里勤奋地做你讨厌的事情，然后才能到达好的部分，但伟大的工作不是这样产生的。伟大的工作是通过持续专注于你真正感兴趣的事情而产生的。当你停下来回顾时，你会惊讶地发现自己已经走了多远。

The reason we’re surprised is that we underestimate the cumulative effect of work. Writing a page a day doesn’t sound like much, but if you do it every day you’ll write a book a year. That’s the key: consistency. People who do great things don’t get a lot done every day. They get something done, rather than nothing.

我们感到惊讶的原因是我们低估了工作的累积效应。每天写一页听起来不多，但如果你每天都这样做，一年就能写出一本书。这就是关键：持续性。做出伟大事业的人并不是每天都完成很多工作。他们是每天都完成一些工作，而不是什么都不做。

If you do work that compounds, you’ll get exponential growth. Most people who do this do it unconsciously, but it’s worth stopping to think about. Learning, for example, is an instance of this phenomenon: the more you learn about something, the easier it is to learn more. Growing an audience is another: the more fans you have, the more new fans they’ll bring you.

如果你做的工作能够复利，你就会获得指数级增长。大多数人在做这种工作时是无意识的，但值得停下来思考一下。例如，学习就是这种现象的一个实例：你对某事了解得越多，就越容易学到更多。培养受众也是如此：你的粉丝越多，他们就会为你带来更多新粉丝。

The trouble with exponential growth is that the curve feels flat in the beginning. It isn’t; it’s still a wonderful exponential curve. But we can’t grasp that intuitively, so we underrate exponential growth in its early stages.

指数增长的问题在于，曲线在开始时感觉是平的。实际上并非如此；它仍然是一条美妙的指数曲线。但我们无法直观地理解这一点，所以我们在早期阶段低估了指数增长。

Something that grows exponentially can become so valuable that it’s worth making an extraordinary effort to get it started. But since we underrate exponential growth early on, this too is mostly done unconsciously: people push through the initial, unrewarding phase of learning something new because they know from experience that learning new things always takes an initial push, or they grow their audience one fan at a time because they have nothing better to do. If people consciously realized they could invest in exponential growth, many more would do it.

一些呈指数增长的事物可能变得如此有价值，以至于值得付出非凡的努力来启动它。但由于我们在早期低估了指数增长，这也大多是无意识地完成的：人们会坚持度过学习新事物初期那个无回报的阶段，因为他们从经验中知道学习新事物总是需要一个初始推动；或者他们一次只增加一个粉丝来培养受众，因为他们没有更好的事情可做。如果人们有意识地意识到他们可以投资于指数增长，会有更多人这样做。

Work doesn’t just happen when you’re trying to. There’s a kind of undirected thinking you do when walking or taking a shower or lying in bed that can be very powerful. By letting your mind wander a little, you’ll often solve problems you were unable to solve by frontal attack.

工作并不只是在你刻意尝试时才会发生。当你散步、洗澡或躺在床上时，会有一种无方向的思考，这种思考可能非常强大。通过让你的思维稍微漫游一下，你常常能解决那些通过正面攻击无法解决的问题。

You have to be working hard in the normal way to benefit from this phenomenon, though. You can’t just walk around daydreaming. The daydreaming has to be interleaved with deliberate work that feeds it questions.

不过，要从这种现象中受益，你还是需要以正常方式努力工作。你不能只是四处走动做白日梦。白日梦必须与有意识的工作交织在一起，后者为前者提供问题。

¹⁰ knows to avoid distractions at work, but it’s also important to avoid them in the other half of the cycle. When you let your mind wander, it wanders to whatever you care about most at that moment. So avoid the kind of distraction that pushes your work out of the top spot, or you’ll waste this valuable type of thinking on the distraction instead. (Exception: Don’t avoid love.)

每个人都知道在工作时要避免分心，但在思维周期的另一半也同样重要。当你让思维漫游时，它会漫游到你当时最关心的事情上。所以要避免那种将你的工作从首要位置挤出去的干扰，否则你会把这种宝贵的思考方式浪费在干扰上。（例外：不要避开爱情。）

Consciously cultivate your taste in the work done in your field. Until you know which is the best and what makes it so, you don’t know what you’re aiming for.

有意识地培养你对本领域工作的品味。在你知道哪些是最好的以及是什么使它们成为最好的之前，你不知道自己的目标是什么。

And that is what you’re aiming for, because if you don’t try to be the best, you won’t even be good. This observation has been made by so many people in so many different fields that it might be worth thinking about why it’s true. It could be because ambition is a phenomenon where almost all the error is in one direction — where almost all the shells that miss the target miss by falling short. Or it could be because ambition to be the best is a qualitatively different thing from ambition to be good. Or maybe being good is simply too vague a standard. Probably all three are true.

而这正是你的目标，因为如果你不尝试成为最好的，你甚至不会变好。这个观察已经被许多不同领域的人提出，也许值得思考为什么它是真的。可能是因为野心是一种几乎所有错误都朝一个方向的现象——几乎所有未命中目标的炮弹都是因为射程不够。或者可能是因为成为最好的野心在质上与成为好的野心不同。或者可能仅仅是因为”好”是一个太模糊的标准。可能这三点都是正确的。

¹¹ there’s a kind of economy of scale here. Though it might seem like you’d be taking on a heavy burden by trying to be the best, in practice you often end up net ahead. It’s exciting, and also strangely liberating. It simplifies things. In some ways it’s easier to try to be the best than to try merely to be good.

幸运的是，这里存在一种规模经济。虽然看起来你试图成为最好的会承担沉重的负担，但实际上你往往会最终获得净收益。这既令人兴奋，又奇怪地让人感到解放。它简化了事情。在某些方面，试图成为最好的比仅仅试图变好更容易。

One way to aim high is to try to make something that people will care about in a hundred years. Not because their opinions matter more than your contemporaries’, but because something that still seems good in a hundred years is more likely to be genuinely good.

瞄准高处的一种方法是尝试创造一些人们在一百年后仍会关心的东西。这不是因为他们的意见比你同时代人的意见更重要，而是因为一百年后仍然看起来好的东西更有可能是真正好的。

Don’t try to work in a distinctive style. Just try to do the best job you can; you won’t be able to help doing it in a distinctive way.

不要试图以独特的风格工作。只需尽你所能做到最好；你会不由自主地以独特的方式做事。

Style is doing things in a distinctive way without trying to. Trying to is affectation.

风格是在不刻意的情况下以独特的方式做事。刻意为之就是做作。

Affectation is in effect to pretend that someone other than you is doing the work. You adopt an impressive but fake persona, and while you’re pleased with the impressiveness, the fakeness is what shows in the work.

做作实际上是假装有人代替你在做工作。你采用一个令人印象深刻但虚假的人格，虽然你对其印象深刻的一面感到满意，但在工作中显现出来的却是其虚假的一面。

¹² temptation to be someone else is greatest for the young. They often feel like nobodies. But you never need to worry about that problem, because it’s self-solving if you work on sufficiently ambitious projects. If you succeed at an ambitious project, you’re not a nobody; you’re the person who did it. So just do the work and your identity will take care of itself.

年轻人最容易受到想要成为别人的诱惑。他们常常觉得自己是无名之辈。但你永远不需要担心这个问题，因为如果你从事足够雄心勃勃的项目，这个问题就会自行解决。如果你在一个雄心勃勃的项目中取得成功，你就不再是无名之辈；你就是完成它的那个人。所以只管做工作，你的身份自然会形成。

“Avoid affectation” is a useful rule so far as it goes, but how would you express this idea positively? How would you say what to be, instead of what not to be? The best answer is earnest. If you’re earnest you avoid not just affectation but a whole set of similar vices.

“避免做作”是一个有用的规则，但你如何积极地表达这个想法呢？你会如何说应该成为什么，而不是不应该成为什么？最好的答案是诚恳。如果你诚恳，你不仅能避免做作，还能避免一整套类似的恶习。

The core of being earnest is being intellectually honest. We’re taught as children to be honest as an unselfish virtue — as a kind of sacrifice. But in fact it’s a source of power too. To see new ideas, you need an exceptionally sharp eye for the truth. You’re trying to see more truth than others have seen so far. And how can you have a sharp eye for the truth if you’re intellectually dishonest?

诚恳的核心是保持智力诚实。我们从小就被教导诚实是一种无私的美德——一种牺牲。但事实上，它也是一种力量的来源。要看到新想法，你需要对真相有异常敏锐的洞察力。你在努力看到比其他人迄今为止看到的更多真相。如果你在智力上不诚实，你怎么能对真相有敏锐的洞察力呢？

One way to avoid intellectual dishonesty is to maintain a slight positive pressure in the opposite direction. Be aggressively willing to admit that you’re mistaken. Once you’ve admitted you were mistaken about something, you’re free. Till then you have to carry it.

避免智力不诚实的一种方法是在相反的方向保持轻微的正压力。积极地愿意承认你的错误。一旦你承认了自己在某事上的错误，你就自由了。在那之前，你必须一直背负着它。

¹³ more subtle component of earnestness is informality. Informality is much more important than its grammatically negative name implies. It’s not merely the absence of something. It means focusing on what matters instead of what doesn’t.

诚恳的另一个更微妙的组成部分是非正式性。非正式性比其语法上的否定名称所暗示的要重要得多。它不仅仅是某些东西的缺失。它意味着专注于重要的事情，而不是不重要的事情。

What formality and affectation have in common is that as well as doing the work, you’re trying to seem a certain way as you’re doing it. But any energy that goes into how you seem comes out of being good. That’s one reason nerds have an advantage in doing great work: they expend little effort on seeming anything. In fact that’s basically the definition of a nerd.

正式性和做作的共同点是，除了做工作之外，你还试图在做工作时表现出某种样子。但任何用于表现的能量都会从做好事情中抽离。这就是书呆子在做伟大工作时有优势的原因之一：他们几乎不花精力去表现什么。事实上，这基本上就是书呆子的定义。

Nerds have a kind of innocent boldness that’s exactly what you need in doing great work. It’s not learned; it’s preserved from childhood. So hold onto it. Be the one who puts things out there rather than the one who sits back and offers sophisticated-sounding criticisms of them. “It’s easy to criticize” is true in the most literal sense, and the route to great work is never easy.

书呆子有一种天真的大胆，这正是你在做伟大工作时所需要的。这不是学来的；而是从童年保留下来的。所以要保持住它。要成为那个把东西拿出来的人，而不是坐在后面对它们提出听起来很高深的批评的人。“批评很容易”在最字面的意义上是真的，而通往伟大工作的道路从来都不容易。

There may be some jobs where it’s an advantage to be cynical and pessimistic, but if you want to do great work it’s an advantage to be optimistic, even though that means you’ll risk looking like a fool sometimes. There’s an old tradition of doing the opposite. The Old Testament says it’s better to keep quiet lest you look like a fool. But that’s advice for seeming smart. If you actually want to discover new things, it’s better to take the risk of telling people your ideas.

可能有些工作中，愤世嫉俗和悲观是一种优势，但如果你想做伟大的工作，乐观是一种优势，尽管这意味着你有时会冒着看起来像个傻瓜的风险。有一个古老的传统是做相反的事。《旧约》说最好保持沉默，以免看起来像个傻瓜。但那是为了看起来聪明的建议。如果你真的想发现新事物，最好冒险告诉人们你的想法。

Some people are naturally earnest, and with others it takes a conscious effort. Either kind of earnestness will suffice. But I doubt it would be possible to do great work without being earnest. It’s so hard to do even if you are. You don’t have enough margin for error to accommodate the distortions introduced by being affected, intellectually dishonest, orthodox, fashionable, or cool.

有些人天生诚恳，而对其他人来说，这需要有意识的努力。这两种诚恳都足够了。但我怀疑如果不诚恳，是不可能做出伟大的工作的。即使你很诚恳，做到这一点也非常困难。你没有足够的错误余地来容纳因做作、智力不诚实、墨守成规、赶时髦或装酷而带来的扭曲。

¹⁴ work is consistent not only with who did it, but with itself. It’s usually all of a piece. So if you face a decision in the middle of working on something, ask which choice is more consistent.

伟大的工作不仅与完成它的人一致，而且与自身一致。它通常是浑然一体的。所以如果你在工作过程中面临一个决定，问问哪个选择更一致。

You may have to throw things away and redo them. You won’t necessarily have to, but you have to be willing to. And that can take some effort; when there’s something you need to redo, status quo bias and laziness will combine to keep you in denial about it. To beat this ask: If I’d already made the change, would I want to revert to what I have now?

你可能需要丢弃一些东西并重做。你不一定必须这样做，但你必须愿意这样做。这可能需要一些努力；当有什么需要重做时，现状偏见和懒惰会结合起来，让你对此保持否认。要克服这一点，可以问自己：如果我已经做出了改变，我会想回到现在的状态吗？

Have the confidence to cut. Don’t keep something that doesn’t fit just because you’re proud of it, or because it cost you a lot of effort.

要有信心去删减。不要仅仅因为你为某样东西感到自豪，或者因为它花费了你很多努力，就保留不合适的东西。

Indeed, in some kinds of work it’s good to strip whatever you’re doing to its essence. The result will be more concentrated; you’ll understand it better; and you won’t be able to lie to yourself about whether there’s anything real there.

事实上，在某些类型的工作中，将你所做的事情剥离到本质是很好的。结果会更加集中；你会更好地理解它；而且你无法对自己撒谎，说那里是否有什么真实的东西。

Mathematical elegance may sound like a mere metaphor, drawn from the arts. That’s what I thought when I first heard the term “elegant” applied to a proof. But now I suspect it’s conceptually prior — that the main ingredient in artistic elegance is mathematical elegance. At any rate it’s a useful standard well beyond math.

数学上的优雅可能听起来只是一个从艺术中借用的比喻。当我第一次听到”优雅”这个词被用于证明时，我就是这么想的。但现在我怀疑它在概念上是先于艺术的——艺术优雅的主要成分是数学优雅。无论如何，它是一个远远超出数学范畴的有用标准。

Elegance can be a long-term bet, though. Laborious solutions will often have more prestige in the short term. They cost a lot of effort and they’re hard to understand, both of which impress people, at least temporarily.

不过，优雅可能是一个长期的赌注。在短期内，费力的解决方案往往会有更多的声望。它们需要付出大量努力，而且难以理解，这两点都会给人留下深刻印象，至少是暂时的。

Whereas some of the very best work will seem like it took comparatively little effort, because it was in a sense already there. It didn’t have to be built, just seen. It’s a very good sign when it’s hard to say whether you’re creating something or discovering it.

而一些最好的工作看起来似乎花费的努力相对较少，因为从某种意义上说，它已经存在了。它不需要被建造，只需要被看到。当你很难说你是在创造还是在发现某样东西时，这是一个很好的迹象。

When you’re doing work that could be seen as either creation or discovery, err on the side of discovery. Try thinking of yourself as a mere conduit through which the ideas take their natural shape.

当你做的工作可以被视为创造或发现时，倾向于发现的一方。试着把自己想象成一个简单的管道，通过它，想法自然地形成。

(Strangely enough, one exception is the problem of choosing a problem to work on. This is usually seen as search, but in the best case it’s more like creating something. In the best case you create the field in the process of exploring it.)

（奇怪的是，有一个例外是选择要解决的问题。这通常被视为搜索，但在最好的情况下，它更像是创造某些东西。在最好的情况下，你在探索过程中创造了这个领域。）

Similarly, if you’re trying to build a powerful tool, make it gratuitously unrestrictive. A powerful tool almost by definition will be used in ways you didn’t expect, so err on the side of eliminating restrictions, even if you don’t know what the benefit will be.

同样，如果你试图构建一个强大的工具，就让它毫无限制。一个强大的工具几乎根据定义会以你意想不到的方式被使用，所以要倾向于消除限制，即使你不知道这样做会有什么好处。

Great work will often be tool-like in the sense of being something others build on. So it’s a good sign if you’re creating ideas that others could use, or exposing questions that others could answer. The best ideas have implications in many different areas.

伟大的工作通常在某种意义上像工具一样，是其他人可以在其基础上构建的东西。所以，如果你创造的想法可以被他人使用，或者提出的问题可以被他人回答，这是一个好兆头。最好的想法在许多不同的领域都有影响。

If you express your ideas in the most general form, they’ll be truer than you intended.

如果你以最一般的形式表达你的想法，它们会比你预期的更加真实。

True by itself is not enough, of course. Great ideas have to be true and new. And it takes a certain amount of ability to see new ideas even once you’ve learned enough to get to one of the frontiers of knowledge.

当然，仅仅是真实还不够。伟大的想法必须是真实的和新颖的。即使你已经学到足够的知识达到了知识的前沿之一，看到新想法也需要一定的能力。

In English we give this ability names like originality, creativity, and imagination. And it seems reasonable to give it a separate name, because it does seem to some extent a separate skill. It’s possible to have a great deal of ability in other respects — to have a great deal of what’s often called technical ability — and yet not have much of this.

在英语中，我们给这种能力起名为原创性、创造力和想象力。给它一个单独的名字似乎是合理的，因为它在某种程度上确实是一种独立的技能。一个人可能在其他方面有很强的能力——拥有通常被称为”技术”能力的东西——但却没有多少这种能力。

I’ve never liked the term “creative process.” It seems misleading. Originality isn’t a process, but a habit of mind. Original thinkers throw off new ideas about whatever they focus on, like an angle grinder throwing off sparks. They can’t help it.

我一直不喜欢”创造性过程”这个词。它似乎有误导性。原创性不是一个过程，而是一种思维习惯。原创性思考者会对他们关注的任何事物产生新想法，就像角磨机产生火花一样。他们无法控制这一点。

If the thing they’re focused on is something they don’t understand very well, these new ideas might not be good. One of the most original thinkers I know decided to focus on dating after he got divorced. He knew roughly as much about dating as the average 15 year old, and the results were spectacularly colorful. But to see originality separated from expertise like that made its nature all the more clear.

如果他们关注的事物是他们不太了解的东西，这些新想法可能不会很好。我认识的一个最有原创性的思考者在离婚后决定专注于约会。他对约会的了解大约和普通15岁的孩子一样多，结果非常丰富多彩。但看到原创性与专业知识如此分离，反而使其本质更加清晰。

I don’t know if it’s possible to cultivate originality, but there are definitely ways to make the most of however much you have. For example, you’re much more likely to have original ideas when you’re working on something. Original ideas don’t come from trying to have original ideas. They come from trying to build or understand something slightly too difficult.

我不知道是否可以培养原创性，但肯定有办法充分利用你所拥有的原创性。例如，当你在做某件事时，你更有可能产生原创性想法。原创性想法不是来自于试图产生原创性想法。它们来自于尝试构建或理解一些稍微有点困难的东西。

¹⁵ or writing about the things you’re interested in is a good way to generate new ideas. When you try to put ideas into words, a missing idea creates a sort of vacuum that draws it out of you. Indeed, there’s a kind of thinking that can only be done by writing.

谈论或写下你感兴趣的事情是产生新想法的好方法。当你试图将想法用语言表达出来时，缺失的想法会创造一种真空，从而将它从你身上吸引出来。事实上，有一种思考只能通过写作来完成。

Changing your context can help. If you visit a new place, you’ll often find you have new ideas there. The journey itself often dislodges them. But you may not have to go far to get this benefit. Sometimes it’s enough just to go for a walk.

改变你的环境可以有所帮助。如果你访问一个新地方，你常常会发现自己在那里有新的想法。旅程本身往往会激发这些想法。但你可能不需要走很远就能获得这种好处。有时只是去散步就足够了。

¹⁶It also helps to travel in topic space. You’ll have more new ideas if you explore lots of different topics, partly because it gives the angle grinder more surface area to work on, and partly because analogies are an especially fruitful source of new ideas.

在主题空间中游历也有帮助。如果你探索很多不同的主题，你会有更多的新想法，部分原因是它给角磨机提供了更多的工作表面，部分原因是类比是新想法的一个特别丰富的来源。

Don’t divide your attention evenly between many topics though, or you’ll spread yourself too thin. You want to distribute it according to something more like a power law.

不过，不要在许多主题之间平均分配你的注意力，否则你会把自己分散得太薄。你应该按照更接近幂律的方式分配注意力。

¹⁷ Be professionally curious about a few topics and idly curious about many more.Curiosity and originality are closely related. Curiosity feeds originality by giving it new things to work on. But the relationship is closer than that. Curiosity is itself a kind of originality; it’s roughly to questions what originality is to answers. And since questions at their best are a big component of answers, curiosity at its best is a creative force.

对少数几个主题保持专业的好奇心，对更多主题保持闲散的好奇心。好奇心和原创性密切相关。好奇心通过给原创性提供新的工作对象来滋养它。但它们的关系比这更密切。好奇心本身就是一种原创性；它对问题的作用大致相当于原创性对答案的作用。而且由于最好的问题是答案的重要组成部分，最好的好奇心是一种创造性的力量。

Having new ideas is a strange game, because it usually consists of seeing things that were right under your nose. Once you’ve seen a new idea, it tends to seem obvious. Why did no one think of this before?

产生新想法是一个奇怪的游戏，因为它通常包括看到就在你眼皮底下的东西。一旦你看到了一个新想法，它往往会显得很明显。为什么以前没有人想到这一点？

When an idea seems simultaneously novel and obvious, it’s probably a good one.

当一个想法同时看起来新颖和显而易见时，它可能是一个好想法。

Seeing something obvious sounds easy. And yet empirically having new ideas is hard. What’s the source of this apparent contradiction? It’s that seeing the new idea usually requires you to change the way you look at the world. We see the world through models that both help and constrain us. When you fix a broken model, new ideas become obvious. But noticing and fixing a broken model is hard. That’s how new ideas can be both obvious and yet hard to discover: they’re easy to see after you do something hard.

看到显而易见的东西听起来很容易。然而，从经验上看，产生新想法是困难的。这种明显矛盾的来源是什么？这是因为看到新想法通常需要你改变看待世界的方式。我们通过既帮助我们又限制我们的模型来看世界。当你修复一个破损的模型时，新想法就变得显而易见了。但注意到并修复一个破损的模型是困难的。这就是新想法既显而易见又难以发现的原因：它们在你做了一些困难的事情之后就容易看到了。

One way to discover broken models is to be stricter than other people. Broken models of the world leave a trail of clues where they bash against reality. Most people don’t want to see these clues. It would be an understatement to say that they’re attached to their current model; it’s what they think in; so they’ll tend to ignore the trail of clues left by its breakage, however conspicuous it may seem in retrospect.

发现破损模型的一种方法是比其他人更严格。世界的破损模型在与现实碰撞的地方留下了一串线索。大多数人不想看到这些线索。说他们依恋于他们当前的模型还是轻描淡写；这是他们思考的方式；所以他们倾向于忽视其破损留下的线索，无论这些线索事后看来多么明显。

To find new ideas you have to seize on signs of breakage instead of looking away. That’s what Einstein did. He was able to see the wild implications of Maxwell’s equations not so much because he was looking for new ideas as because he was stricter.

要找到新想法，你必须抓住破损的迹象，而不是视而不见。这就是爱因斯坦所做的。他能够看到麦克斯韦方程的疯狂含义，不是因为他在寻找新想法，而是因为他更严格。

The other thing you need is a willingness to break rules. Paradoxical as it sounds, if you want to fix your model of the world, it helps to be the sort of person who’s comfortable breaking rules. From the point of view of the old model, which everyone including you initially shares, the new model usually breaks at least implicit rules.

你需要的另一件事是打破规则的意愿。虽然听起来矛盾，但如果你想修复你的世界模型，成为那种乐于打破规则的人会有所帮助。从最初包括你在内的每个人都共享的旧模型的角度来看，新模型通常至少会打破一些隐含的规则。

Few understand the degree of rule-breaking required, because new ideas seem much more conservative once they succeed. They seem perfectly reasonable once you’re using the new model of the world they brought with them. But they didn’t at the time; it took the greater part of a century for the heliocentric model to be generally accepted, even among astronomers, because it felt so wrong.

很少有人理解所需的破坏规则的程度，因为新想法一旦成功就显得保守得多。一旦你使用它们带来的新世界模型，它们就显得完全合理。但当时并非如此；日心说模型花了近一个世纪的时间才被普遍接受，即使在天文学家中也是如此，因为它感觉如此错误。

Indeed, if you think about it, a good new idea has to seem bad to most people, or someone would have already explored it. So what you’re looking for is ideas that seem crazy, but the right kind of crazy. How do you recognize these? You can’t with certainty. Often ideas that seem bad are bad. But ideas that are the right kind of crazy tend to be exciting; they’re rich in implications; whereas ideas that are merely bad tend to be depressing.

事实上，如果你仔细想想，一个好的新想法对大多数人来说必须看起来是坏的，否则有人就已经探索过它了。所以你要寻找的是那些看起来疯狂，但是正确类型的疯狂的想法。你如何识别这些？你无法确定。通常看起来坏的想法确实是坏的。但正确类型的疯狂想法往往令人兴奋；它们富有含义；而仅仅是坏的想法往往令人沮丧。

There are two ways to be comfortable breaking rules: to enjoy breaking them, and to be indifferent to them. I call these two cases being aggressively and passively independent-minded.

有两种方式可以让人在打破规则时感到自在：享受打破规则的过程，或者对规则漠不关心。我把这两种情况称为主动独立思考和被动独立思考。

The aggressively independent-minded are the naughty ones. Rules don’t merely fail to stop them; breaking rules gives them additional energy. For this sort of person, delight at the sheer audacity of a project sometimes supplies enough activation energy to get it started.

主动独立思考的人是调皮的那一类。规则不仅无法阻止他们；打破规则反而给他们额外的能量。对这类人来说，一个项目的纯粹大胆有时能提供足够的激活能量来启动它。

The other way to break rules is not to care about them, or perhaps even to know they exist. This is why novices and outsiders often make new discoveries; their ignorance of a field’s assumptions acts as a source of temporary passive independent-mindedness. Aspies also seem to have a kind of immunity to conventional beliefs. Several I know say that this helps them to have new ideas.

打破规则的另一种方式是不在乎它们，或者甚至不知道它们的存在。这就是为什么新手和局外人经常能做出新发现；他们对某个领域假设的无知充当了一种临时的被动独立思考的来源。阿斯伯格症患者似乎也对传统信念有一种免疫力。我认识的几个人说，这帮助他们产生新想法。

Strictness plus rule-breaking sounds like a strange combination. In popular culture they’re opposed. But popular culture has a broken model in this respect. It implicitly assumes that issues are trivial ones, and in trivial matters strictness and rule-breaking are opposed. But in questions that really matter, only rule-breakers can be truly strict.

严格加上打破规则听起来是一个奇怪的组合。在流行文化中，它们是对立的。但在这方面，流行文化有一个错误的模型。它隐含地假设问题都是琐碎的，而在琐碎的事情上，严格和打破规则确实是对立的。但在真正重要的问题上，只有打破规则的人才能真正严格。

An overlooked idea often doesn’t lose till the semifinals. You do see it, subconsciously, but then another part of your subconscious shoots it down because it would be too weird, too risky, too much work, too controversial. This suggests an exciting possibility: if you could turn off such filters, you could see more new ideas.

一个被忽视的想法通常不会在半决赛前就被淘汰。你确实在潜意识中看到了它，但然后你潜意识的另一部分又将其否决了，因为它太奇怪、太冒险、太费力或太有争议。这暗示了一个令人兴奋的可能性：如果你能关闭这些过滤器，你就能看到更多新想法。

One way to do that is to ask what would be good ideas for someone else to explore. Then your subconscious won’t shoot them down to protect you.

实现这一点的一种方法是问问什么样的想法适合别人去探索。这样你的潜意识就不会为了保护你而否决它们。

You could also discover overlooked ideas by working in the other direction: by starting from what’s obscuring them. Every cherished but mistaken principle is surrounded by a dead zone of valuable ideas that are unexplored because they contradict it.

你也可以通过反向工作来发现被忽视的想法：从遮蔽它们的东西开始。每一个被珍视但错误的原则周围都有一个死区，里面充满了有价值但未被探索的想法，因为它们与之矛盾。

Religions are collections of cherished but mistaken principles. So anything that can be described either literally or metaphorically as a religion will have valuable unexplored ideas in its shadow. Copernicus and Darwin both made discoveries of this type.

宗教是一系列被珍视但错误的原则的集合。所以任何可以字面上或比喻性地被描述为宗教的东西，在其阴影中都会有有价值的未被探索的想法。哥白尼和达尔文都做出了这种类型的发现。

¹⁸What are people in your field religious about, in the sense of being too attached to some principle that might not be as self-evident as they think? What becomes possible if you discard it?

在你的领域里，人们对什么有”宗教信仰”，即过于依附于某些可能并不像他们认为的那样不言自明的原则？如果你抛弃它，会有什么可能性？

People show much more originality in solving problems than in deciding which problems to solve. Even the smartest can be surprisingly conservative when deciding what to work on. People who’d never dream of being fashionable in any other way get sucked into working on fashionable problems.

人们在解决问题时表现出的原创性远远超过决定解决哪些问题时的原创性。即使是最聪明的人，在决定要做什么工作时也可能出人意料地保守。那些在其他方面从不梦想追随时尚的人，却被吸引去研究时髦的问题。

One reason people are more conservative when choosing problems than solutions is that problems are bigger bets. A problem could occupy you for years, while exploring a solution might only take days. But even so I think most people are too conservative. They’re not merely responding to risk, but to fashion as well. Unfashionable problems are undervalued.

人们在选择问题时比选择解决方案时更保守的一个原因是，问题是更大的赌注。一个问题可能会占用你数年时间，而探索一个解决方案可能只需要几天。但即便如此，我认为大多数人还是太保守了。他们不仅仅是在应对风险，也在追随时尚。不时髦的问题被低估了。

One of the most interesting kinds of unfashionable problem is the problem that people think has been fully explored, but hasn’t. Great work often takes something that already exists and shows its latent potential. Durer and Watt both did this. So if you’re interested in a field that others think is tapped out, don’t let their skepticism deter you. People are often wrong about this.

最有趣的一种不时髦问题是那些人们认为已经被充分探索过，但实际上并非如此的问题。伟大的工作常常是取一些已经存在的东西，并展示其潜在的可能性。杜勒和瓦特都做到了这一点。所以如果你对一个别人认为已经被榨干的领域感兴趣，不要让他们的怀疑阻止你。人们在这方面常常是错的。

Working on an unfashionable problem can be very pleasing. There’s no hype or hurry. Opportunists and critics are both occupied elsewhere. The existing work often has an old-school solidity. And there’s a satisfying sense of economy in cultivating ideas that would otherwise be wasted.

研究一个不时髦的问题可能会非常令人愉快。没有炒作或匆忙。机会主义者和批评者都忙于其他地方。现有的工作常常有一种老派的扎实感。而且，在培养那些原本会被浪费的想法时，会有一种令人满意的经济感。

But the most common type of overlooked problem is not explicitly unfashionable in the sense of being out of fashion. It just doesn’t seem to matter as much as it actually does. How do you find these? By being self-indulgent — by letting your curiosity have its way, and tuning out, at least temporarily, the little voice in your head that says you should only be working on “important” problems.

但最常见的被忽视问题类型并不是明确地不时髦，即不是那种过时的意思。它只是看起来没有实际那么重要。你如何找到这些问题？通过自我放纵——让你的好奇心自由发挥，至少暂时地忽略掉你脑海中那个说你应该只研究”重要”问题的小声音。

You do need to work on important problems, but almost everyone is too conservative about what counts as one. And if there’s an important but overlooked problem in your neighborhood, it’s probably already on your subconscious radar screen. So try asking yourself: if you were going to take a break from “serious” work to work on something just because it would be really interesting, what would you do? The answer is probably more important than it seems.

你确实需要研究重要的问题，但几乎每个人对什么算作重要问题的判断都过于保守。如果在你的领域里有一个重要但被忽视的问题，它可能已经在你的潜意识雷达屏幕上了。所以试着问问自己：如果你要从”严肃”的工作中抽身出来，只是因为某件事真的很有趣而去做它，你会做什么？答案可能比看起来更重要。

Originality in choosing problems seems to matter even more than originality in solving them. That’s what distinguishes the people who discover whole new fields. So what might seem to be merely the initial step — deciding what to work on — is in a sense the key to the whole game.

在选择问题时的原创性似乎比解决问题时的原创性更重要。这就是那些发现全新领域的人与众不同的地方。所以，看似只是初始步骤的东西——决定要研究什么——在某种意义上是整个游戏的关键。

Few grasp this. One of the biggest misconceptions about new ideas is about the ratio of question to answer in their composition. People think big ideas are answers, but often the real insight was in the question.

很少有人理解这一点。关于新想法的最大误解之一是关于其组成中问题与答案的比例。人们认为大想法是答案，但通常真正的洞见在于问题本身。

Part of the reason we underrate questions is the way they’re used in schools. In schools they tend to exist only briefly before being answered, like unstable particles. But a really good question can be much more than that. A really good question is a partial discovery. How do new species arise? Is the force that makes objects fall to earth the same as the one that keeps planets in their orbits? By even asking such questions you were already in excitingly novel territory.

我们低估问题的部分原因是它们在学校中的使用方式。在学校里，问题往往只是短暂存在就被回答了，就像不稳定的粒子。但一个真正好的问题可以远不止于此。一个真正好的问题就是一个部分的发现。新物种是如何产生的？使物体落向地球的力是否与保持行星在轨道上运行的力相同？仅仅是提出这样的问题，你就已经进入了令人兴奋的新领域。

Unanswered questions can be uncomfortable things to carry around with you. But the more you’re carrying, the greater the chance of noticing a solution — or perhaps even more excitingly, noticing that two unanswered questions are the same.

未回答的问题可能是令人不舒服的东西，让你一直带着它们。但你携带的越多，注意到解决方案的机会就越大——或者更令人兴奋的是，注意到两个未回答的问题其实是同一个。

Sometimes you carry a question for a long time. Great work often comes from returning to a question you first noticed years before — in your childhood, even — and couldn’t stop thinking about. People talk a lot about the importance of keeping your youthful dreams alive, but it’s just as important to keep your youthful questions alive.

有时你会长期携带一个问题。伟大的工作常常来自于回到你多年前——甚至在童年时期——首次注意到并一直无法停止思考的问题。人们经常谈论保持年轻梦想的重要性，但保持年轻时的问题同样重要。

¹⁹ This is one of the places where actual expertise differs most from the popular picture of it. In the popular picture, experts are certain. But actually the more puzzled you are, the better, so long as (a) the things you’re puzzled about matter, and (b) no one else understands them either.

这是实际专业知识与其流行印象最不同的地方之一。在流行的印象中，专家是确定的。但实际上，你越困惑越好，只要（a）你困惑的事情很重要，而且（b）其他人也不理解这些事情。

Think about what’s happening at the moment just before a new idea is discovered. Often someone with sufficient expertise is puzzled about something. Which means that originality consists partly of puzzlement — of confusion! You have to be comfortable enough with the world being full of puzzles that you’re willing to see them, but not so comfortable that you don’t want to solve them.

想想在一个新想法被发现的前一刻发生了什么。通常是一个有足够专业知识的人对某事感到困惑。这意味着原创性部分由困惑组成——由混乱组成！你必须对充满谜题的世界感到足够舒适，愿意看到这些谜题，但又不能舒适到不想解决它们。

²⁰It’s a great thing to be rich in unanswered questions. And this is one of those situations where the rich get richer, because the best way to acquire new questions is to try answering existing ones. Questions don’t just lead to answers, but also to more questions.

拥有大量未回答的问题是一件很棒的事。这是那种富者愈富的情况之一，因为获得新问题的最好方法是尝试回答现有的问题。问题不仅导向答案，还导向更多的问题。

The best questions grow in the answering. You notice a thread protruding from the current paradigm and try pulling on it, and it just gets longer and longer. So don’t require a question to be obviously big before you try answering it. You can rarely predict that. It’s hard enough even to notice the thread, let alone to predict how much will unravel if you pull on it.

最好的问题在回答过程中会不断发展。你注意到当前范式中突出的一个线头，试图拉它，它就变得越来越长。所以在尝试回答一个问题之前，不要要求它明显很大。你很难预测这一点。仅仅是注意到这个线头就已经够难的了，更不用说预测拉它会解开多少东西。

It’s better to be promiscuously curious — to pull a little bit on a lot of threads, and see what happens. Big things start small. The initial versions of big things were often just experiments, or side projects, or talks, which then grew into something bigger. So start lots of small things.

最好的问题在回答过程中会不断发展。你注意到当前范式中突出的一个线头，试图拉它，它就变得越来越长。所以在尝试回答一个问题之前，不要要求它明显很大。你很难预测这一点。仅仅是注意到这个线头就已经够难的了，更不用说预测拉它会解开多少东西。

Being prolific is underrated. The more different things you try, the greater the chance of discovering something new. Understand, though, that trying lots of things will mean trying lots of things that don’t work. You can’t have a lot of good ideas without also having a lot of bad ones.

多产是被低估的。你尝试的不同事物越多，发现新事物的机会就越大。不过，要理解，尝试很多事情意味着会尝试很多不成功的事情。你不可能有很多好主意而没有很多坏主意。

²¹Though it sounds more responsible to begin by studying everything that’s been done before, you’ll learn faster and have more fun by trying stuff. And you’ll understand previous work better when you do look at it. So err on the side of starting. Which is easier when starting means starting small; those two ideas fit together like two puzzle pieces.

虽然从研究以前所有已经完成的工作开始听起来更负责任，但通过尝试你会学得更快，也会更有乐趣。而且当你确实去看以前的工作时，你会更好地理解它。所以要倾向于开始行动。当开始意味着从小处着手时，这会更容易；这两个想法就像两块拼图一样契合。

How do you get from starting small to doing something great? By making successive versions. Great things are almost always made in successive versions. You start with something small and evolve it, and the final version is both cleverer and more ambitious than anything you could have planned.

你如何从小处着手发展到做出伟大的事情？通过制作连续的版本。伟大的事物几乎总是通过连续的版本制作而成。你从小事开始，然后不断发展它，最终版本比你能计划的任何东西都更聪明、更有雄心。

It’s particularly useful to make successive versions when you’re making something for people — to get an initial version in front of them quickly, and then evolve it based on their response.

当你为人们制作某些东西时，制作连续版本特别有用——快速将初始版本呈现给他们，然后根据他们的反应进行改进。

Begin by trying the simplest thing that could possibly work. Surprisingly often, it does. If it doesn’t, this will at least get you started.

从尝试可能有效的最简单的事情开始。令人惊讶的是，这种方法经常有效。即使不行，至少也能让你开始行动。

Don’t try to cram too much new stuff into any one version. There are names for doing this with the first version (taking too long to ship) and the second (the second system effect), but these are both merely instances of a more general principle.

不要试图在任何一个版本中塞入太多新东西。对第一个版本（花太长时间才能发布）和第二个版本（第二系统效应）这样做都有专门的名称，但这些只是一个更普遍原则的具体实例。

An early version of a new project will sometimes be dismissed as a toy. It’s a good sign when people do this. That means it has everything a new idea needs except scale, and that tends to follow.

一个新项目的早期版本有时会被当作玩具而被忽视。当人们这样做时，这其实是一个好兆头。这意味着它拥有一个新想法所需的一切，除了规模，而规模往往会随之而来。

²²The alternative to starting with something small and evolving it is to plan in advance what you’re going to do. And planning does usually seem the more responsible choice. It sounds more organized to say “we’re going to do x and then y and then z” than “we’re going to try x and see what happens.” And it is more organized; it just doesn’t work as well.

从小处着手并不断发展的替代方案是提前计划你要做什么。计划通常看起来是更负责任的选择。说”我们要先做x，然后做y，再做z”听起来比”我们要试试x，看看会发生什么”更有条理。它确实更有条理；只是效果不那么好。

Planning per se isn’t good. It’s sometimes necessary, but it’s a necessary evil — a response to unforgiving conditions. It’s something you have to do because you’re working with inflexible media, or because you need to coordinate the efforts of a lot of people. If you keep projects small and use flexible media, you don’t have to plan as much, and your designs can evolve instead.

计划本身并不好。它有时是必要的，但它是一种必要的邪恶——是对严苛条件的回应。你之所以必须这么做，是因为你在使用不灵活的媒介，或者因为你需要协调许多人的努力。如果你保持项目规模小，使用灵活的媒介，你就不需要做那么多计划，你的设计可以进化发展。

Take as much risk as you can afford. In an efficient market, risk is proportionate to reward, so don’t look for certainty, but for a bet with high expected value. If you’re not failing occasionally, you’re probably being too conservative.

承担你能承受的最大风险。在一个高效的市场中，风险与回报成正比，所以不要寻求确定性，而要寻找预期价值高的赌注。如果你从不失败，你可能太保守了。

Though conservatism is usually associated with the old, it’s the young who tend to make this mistake. Inexperience makes them fear risk, but it’s when you’re young that you can afford the most.

虽然保守通常与年长者联系在一起，但年轻人往往更容易犯这个错误。缺乏经验使他们害怕风险，但恰恰是在年轻时，你能承担最多的风险。

Even a project that fails can be valuable. In the process of working on it, you’ll have crossed territory few others have seen, and encountered questions few others have asked. And there’s probably no better source of questions than the ones you encounter in trying to do something slightly too hard.

即使是失败的项目也可能有价值。在工作过程中，你会跨越很少有人见过的领域，遇到很少有人问过的问题。而且，可能没有比在尝试做一些稍微超出能力的事情时遇到的问题更好的问题来源了。

Use the advantages of youth when you have them, and the advantages of age once you have those. The advantages of youth are energy, time, optimism, and freedom. The advantages of age are knowledge, efficiency, money, and power. With effort you can acquire some of the latter when young and keep some of the former when old.

当你年轻时，要利用年轻的优势；当你年长时，要利用年长的优势。年轻的优势是精力、时间、乐观和自由。年长的优势是知识、效率、金钱和权力。通过努力，你可以在年轻时获得一些后者的优势，在年老时保持一些前者的优势。

The old also have the advantage of knowing which advantages they have. The young often have them without realizing it. The biggest is probably time. The young have no idea how rich they are in time. The best way to turn this time to advantage is to use it in slightly frivolous ways: to learn about something you don’t need to know about, just out of curiosity, or to try building something just because it would be cool, or to become freakishly good at something.

年长者还有一个优势，就是知道自己拥有哪些优势。年轻人往往拥有这些优势却没有意识到。最大的优势可能是时间。年轻人不知道他们在时间上有多么富有。利用这些时间的最好方法是稍微轻率地使用它：出于好奇去学习一些你不需要知道的东西，或者仅仅因为很酷就尝试建造某些东西，或者在某方面变得异常优秀。

That “slightly” is an important qualification. Spend time lavishly when you’re young, but don’t simply waste it. There’s a big difference between doing something you worry might be a waste of time and doing something you know for sure will be. The former is at least a bet, and possibly a better one than you think.

那个”稍微”是一个重要的限定词。年轻时要慷慨地花费时间，但不要简单地浪费它。做一些你担心可能是浪费时间的事情和做一些你确定会浪费时间的事情之间有很大的区别。前者至少是一个赌注，可能比你想象的更好。

²³The most subtle advantage of youth, or more precisely of inexperience, is that you’re seeing everything with fresh eyes. When your brain embraces an idea for the first time, sometimes the two don’t fit together perfectly. Usually the problem is with your brain, but occasionally it’s with the idea. A piece of it sticks out awkwardly and jabs you when you think about it. People who are used to the idea have learned to ignore it, but you have the opportunity not to.

年轻的最微妙的优势，或者更准确地说是缺乏经验的优势，是你用全新的眼光看待一切。当你的大脑第一次接受一个想法时，有时两者并不完全契合。通常问题出在你的大脑上，但有时问题出在想法本身。它的某个部分会突兀地凸显出来，当你思考它时会刺痛你。习惯了这个想法的人已经学会忽视它，但你有机会不这样做。

²⁴So when you’re learning about something for the first time, pay attention to things that seem wrong or missing. You’ll be tempted to ignore them, since there’s a 99% chance the problem is with you. And you may have to set aside your misgivings temporarily to keep progressing. But don’t forget about them. When you’ve gotten further into the subject, come back and check if they’re still there. If they’re still viable in the light of your present knowledge, they probably represent an undiscovered idea.

所以当你第一次学习某些东西时，要注意那些看起来错误或缺失的地方。你会倾向于忽视它们，因为有99%的可能性问题出在你身上。你可能需要暂时搁置你的疑虑以继续前进。但不要忘记它们。当你在这个主题上更深入时，回来检查它们是否仍然存在。如果在你现有知识的基础上它们仍然站得住脚，它们可能代表了一个未被发现的想法。

One of the most valuable kinds of knowledge you get from experience is to know what you don’t have to worry about. The young know all the things that could matter, but not their relative importance. So they worry equally about everything, when they should worry much more about a few things and hardly at all about the rest.

从经验中获得的最有价值的知识之一是知道你不需要担心什么。年轻人知道所有可能重要的事情，但不知道它们的相对重要性。所以他们对所有事情都同等担心，而实际上他们应该对少数几件事非常担心，对其余的几乎不用担心。

But what you don’t know is only half the problem with inexperience. The other half is what you do know that ain’t so. You arrive at adulthood with your head full of nonsense — bad habits you’ve acquired and false things you’ve been taught — and you won’t be able to do great work till you clear away at least the nonsense in the way of whatever type of work you want to do.

但你不知道的只是缺乏经验问题的一半。另一半是你知道的那些实际上并非如此的事情。你进入成年期时，头脑中充满了废话——你获得的坏习惯和被教导的错误事物——直到你至少清除掉阻碍你想做的那种工作的废话，你才能做出伟大的工作。

Much of the nonsense left in your head is left there by schools. We’re so used to schools that we unconsciously treat going to school as identical with learning, but in fact schools have all sorts of strange qualities that warp our ideas about learning and thinking.

留在你头脑中的大部分废话是由学校留下的。我们如此习惯于学校，以至于我们无意识地将上学等同于学习，但实际上学校有各种奇怪的特质，扭曲了我们对学习和思考的看法。

For example, schools induce passivity. Since you were a small child, there was an authority at the front of the class telling all of you what you had to learn and then measuring whether you did. But neither classes nor tests are intrinsic to learning; they’re just artifacts of the way schools are usually designed.

例如，学校会诱导被动性。从你还是个小孩子开始，就有一个权威站在教室前面告诉你们所有人必须学什么，然后测量你们是否学会了。但无论是课程还是考试都不是学习的内在要素；它们只是学校通常设计方式的产物。

The sooner you overcome this passivity, the better. If you’re still in school, try thinking of your education as your project, and your teachers as working for you rather than vice versa. That may seem a stretch, but it’s not merely some weird thought experiment. It’s the truth economically, and in the best case it’s the truth intellectually as well. The best teachers don’t want to be your bosses. They’d prefer it if you pushed ahead, using them as a source of advice, rather than being pulled by them through the material.

你越早克服这种被动性越好。如果你还在学校，试着把你的教育看作是你的项目，把你的老师看作是为你工作，而不是相反。这可能看起来有点牵强，但这不仅仅是一个奇怪的思想实验。从经济角度来说，这是事实，在最好的情况下，从智力角度来说也是事实。最好的老师不想成为你的老板。他们更希望你主动前进，把他们作为建议的来源，而不是被他们拉着走过教材。

Schools also give you a misleading impression of what work is like. In school they tell you what the problems are, and they’re almost always soluble using no more than you’ve been taught so far. In real life you have to figure out what the problems are, and you often don’t know if they’re soluble at all.

学校还给你一个关于工作的误导性印象。在学校里，他们告诉你问题是什么，而且这些问题几乎总是可以用你到目前为止所学的知识来解决。在现实生活中，你必须自己弄清楚问题是什么，而且你常常不知道它们是否可以解决。

But perhaps the worst thing schools do to you is train you to win by hacking the test. You can’t do great work by doing that. You can’t trick God. So stop looking for that kind of shortcut. The way to beat the system is to focus on problems and solutions that others have overlooked, not to skimp on the work itself.

但也许学校对你做的最糟糕的事情是训练你通过破解考试来获胜。你不能通过这种方式做出伟大的工作。你不能欺骗上帝。所以停止寻找那种捷径。击败系统的方法是专注于他人忽视的问题和解决方案，而不是在工作本身上偷工减料。

Don’t think of yourself as dependent on some gatekeeper giving you a “big break.” Even if this were true, the best way to get it would be to focus on doing good work rather than chasing influential people.

不要认为自己依赖于某个看门人给你一个”大机会”。即使这是真的，获得它的最好方法也是专注于做好工作，而不是追逐有影响力的人。

And don’t take rejection by committees to heart. The qualities that impress admissions officers and prize committees are quite different from those required to do great work. The decisions of selection committees are only meaningful to the extent that they’re part of a feedback loop, and very few are.

不要把委员会的拒绝放在心上。给招生官和奖项委员会留下深刻印象的品质与做出伟大工作所需的品质大不相同。选拔委员会的决定只有在它们是反馈循环的一部分时才有意义，而很少有这样的情况。

People new to a field will often copy existing work. There’s nothing inherently bad about that. There’s no better way to learn how something works than by trying to reproduce it. Nor does copying necessarily make your work unoriginal. Originality is the presence of new ideas, not the absence of old ones.

刚进入一个领域的人常常会模仿现有的工作。这本身并没有什么不好。没有比尝试复制某样东西更好的方法来学习它是如何运作的了。复制也不一定会使你的工作缺乏原创性。原创性是新想法的存在，而不是旧想法的缺失。

There’s a good way to copy and a bad way. If you’re going to copy something, do it openly instead of furtively, or worse still, unconsciously. This is what’s meant by the famously misattributed phrase “Great artists steal.” The really dangerous kind of copying, the kind that gives copying a bad name, is the kind that’s done without realizing it, because you’re nothing more than a train running on tracks laid down by someone else. But at the other extreme, copying can be a sign of superiority rather than subordination.

有好的复制方式，也有坏的复制方式。如果你要复制某样东西，要公开地做，而不是偷偷摸摸地做，更糟糕的是无意识地做。这就是那句被错误归属的名言”伟大的艺术家偷窃”的含义。真正危险的复制类型，那种给复制带来坏名声的类型，是在不知不觉中进行的复制，因为你只不过是在别人铺设的轨道上行驶的火车。但在另一个极端，复制可能是优越性而非从属性的标志。

²⁵In many fields it’s almost inevitable that your early work will be in some sense based on other people’s. Projects rarely arise in a vacuum. They’re usually a reaction to previous work. When you’re first starting out, you don’t have any previous work; if you’re going to react to something, it has to be someone else’s. Once you’re established, you can react to your own. But while the former gets called derivative and the latter doesn’t, structurally the two cases are more similar than they seem.

在许多领域，你的早期工作几乎不可避免地会在某种意义上基于他人的工作。项目很少凭空产生。它们通常是对先前工作的反应。当你刚开始时，你没有任何先前的工作；如果你要对某事做出反应，那必须是别人的工作。一旦你站稳脚跟，你就可以对自己的工作做出反应。但虽然前者被称为衍生，而后者不被称为衍生，但从结构上看，这两种情况比看起来更相似。

Oddly enough, the very novelty of the most novel ideas sometimes makes them seem at first to be more derivative than they are. New discoveries often have to be conceived initially as variations of existing things, even by their discoverers, because there isn’t yet the conceptual vocabulary to express them.

奇怪的是，最新颖的想法的新颖性有时反而会让它们一开始看起来比实际更具衍生性。新发现常常必须最初被构想为现有事物的变体，甚至是由它们的发现者这样构想，因为还没有概念词汇来表达它们。

There are definitely some dangers to copying, though. One is that you’ll tend to copy old things — things that were in their day at the frontier of knowledge, but no longer are.

不过，复制确实存在一些危险。其中之一是你会倾向于复制旧事物——那些在当时处于知识前沿，但现在已不再如此的事物。

And when you do copy something, don’t copy every feature of it. Some will make you ridiculous if you do. Don’t copy the manner of an eminent 50 year old professor if you’re 18, for example, or the idiom of a Renaissance poem hundreds of years later.

当你确实复制某样东西时，不要复制它的每一个特征。有些特征如果你复制了会让你显得可笑。例如，如果你18岁，就不要模仿一位50岁的著名教授的举止，也不要在几百年后模仿文艺复兴时期诗歌的习语。

Some of the features of things you admire are flaws they succeeded despite. Indeed, the features that are easiest to imitate are the most likely to be the flaws.

你所欣赏的事物的某些特征是它们尽管存在却仍然成功的缺陷。事实上，最容易模仿的特征最有可能是缺陷。

This is particularly true for behavior. Some talented people are jerks, and this sometimes makes it seem to the inexperienced that being a jerk is part of being talented. It isn’t; being talented is merely how they get away with it.

这对行为尤其如此。一些有才能的人是混蛋，这有时会让没有经验的人觉得成为混蛋是有才能的一部分。事实并非如此；有才能只是他们得以逃脱的方式。

One of the most powerful kinds of copying is to copy something from one field into another. History is so full of chance discoveries of this type that it’s probably worth giving chance a hand by deliberately learning about other kinds of work. You can take ideas from quite distant fields if you let them be metaphors.

最强大的复制类型之一是将某样东西从一个领域复制到另一个领域。历史上充满了这种类型的偶然发现，以至于值得通过有意识地学习其他类型的工作来给机会一个帮助。如果你让它们成为隐喻，你可以从相当遥远的领域获取想法。

Negative examples can be as inspiring as positive ones. In fact you can sometimes learn more from things done badly than from things done well; sometimes it only becomes clear what’s needed when it’s missing.

If a lot of the best people in your field are collected in one place, it’s usually a good idea to visit for a while. It will increase your ambition, and also, by showing you that these people are human, increase your self-confidence.

负面例子可以和正面例子一样具有启发性。事实上，你有时可以从做得不好的事情中学到比做得好的事情更多；有时只有当某样东西缺失时，才能清楚地知道需要什么。

²⁶If you’re earnest you’ll probably get a warmer welcome than you might expect. Most people who are very good at something are happy to talk about it with anyone who’s genuinely interested. If they’re really good at their work, then they probably have a hobbyist’s interest in it, and hobbyists always want to talk about their hobbies.

如果你是真诚的，你可能会得到比你预期更热情的欢迎。大多数在某方面非常优秀的人都乐于与任何真正感兴趣的人讨论它。如果他们真的很擅长自己的工作，那么他们可能对它有业余爱好者的兴趣，而业余爱好者总是想谈论他们的爱好。

It may take some effort to find the people who are really good, though. Doing great work has such prestige that in some places, particularly universities, there’s a polite fiction that everyone is engaged in it. And that is far from true. People within universities can’t say so openly, but the quality of the work being done in different departments varies immensely. Some departments have people doing great work; others have in the past; others never have.

不过，找到真正优秀的人可能需要一些努力。做出伟大工作具有如此高的声望，以至于在某些地方，特别是大学，有一种礼貌性的虚构，认为每个人都在从事伟大工作。而这远非事实。大学内部的人不能公开这么说，但不同部门所做工作的质量差异巨大。有些部门有人在做伟大的工作；有些在过去做过；还有些从未做过。

Seek out the best colleagues. There are a lot of projects that can’t be done alone, and even if you’re working on one that can be, it’s good to have other people to encourage you and to bounce ideas off.

寻找最好的同事。有很多项目无法独自完成，即使你正在做一个可以独自完成的项目，有其他人鼓励你并与你交流想法也是很好的。

Colleagues don’t just affect your work, though; they also affect you. So work with people you want to become like, because you will.

然而，同事不仅影响你的工作；他们也影响你这个人。所以要和你想成为的那种人一起工作，因为你会变成那样。

Quality is more important than quantity in colleagues. It’s better to have one or two great ones than a building full of pretty good ones. In fact it’s not merely better, but necessary, judging from history: the degree to which great work happens in clusters suggests that one’s colleagues often make the difference between doing great work and not.

在同事方面，质量比数量更重要。有一两个优秀的同事比有一栋楼的还不错的同事要好。事实上，这不仅仅是更好，而且是必要的，从历史来看：伟大的工作往往以集群方式出现，这表明同事常常是决定是否能做出伟大工作的关键因素。

How do you know when you have sufficiently good colleagues? In my experience, when you do, you know. Which means if you’re unsure, you probably don’t. But it may be possible to give a more concrete answer than that. Here’s an attempt: sufficiently good colleagues offer surprising insights. They can see and do things that you can’t. So if you have a handful of colleagues good enough to keep you on your toes in this sense, you’re probably over the threshold.

你如何知道你有足够好的同事？根据我的经验，当你有时，你就会知道。这意味着如果你不确定，你可能就没有。但也许可以给出一个更具体的答案。这里是一个尝试：足够好的同事能提供令人惊讶的见解。他们能看到和做到你做不到的事情。所以如果你有几个足以让你在这个意义上保持警惕的同事，你可能已经超过了门槛。

Most of us can benefit from collaborating with colleagues, but some projects require people on a larger scale, and starting one of those is not for everyone. If you want to run a project like that, you’ll have to become a manager, and managing well takes aptitude and interest like any other kind of work. If you don’t have them, there is no middle path: you must either force yourself to learn management as a second language, or avoid such projects.

我们大多数人都能从与同事合作中受益，但有些项目需要更大规模的人员，而启动这样的项目并不适合每个人。如果你想运行这样的项目，你就必须成为一个管理者，而良好的管理需要像其他任何工作一样的才能和兴趣。如果你没有这些，就没有中间道路：你要么强迫自己学习管理作为第二语言，要么避开这样的项目。

²⁷Husband your morale. It’s the basis of everything when you’re working on ambitious projects. You have to nurture and protect it like a living organism.

珍惜你的士气。当你在从事雄心勃勃的项目时，它是一切的基础。你必须像照顾一个活的有机体一样培养和保护它。

Morale starts with your view of life. You’re more likely to do great work if you’re an optimist, and more likely to if you think of yourself as lucky than if you think of yourself as a victim.

士气始于你对生活的看法。如果你是一个乐观主义者，你更有可能做出伟大的工作，如果你认为自己是幸运的，而不是认为自己是受害者，你也更有可能做出伟大的工作。

Indeed, work can to some extent protect you from your problems. If you choose work that’s pure, its very difficulties will serve as a refuge from the difficulties of everyday life. If this is escapism, it’s a very productive form of it, and one that has been used by some of the greatest minds in history.

事实上，工作在某种程度上可以保护你免受问题的困扰。如果你选择纯粹的工作，它的困难本身就会成为你逃避日常生活困难的避难所。如果这是逃避主义，那也是一种非常有成效的逃避形式，历史上一些最伟大的头脑都曾使用过这种方式。

Morale compounds via work: high morale helps you do good work, which increases your morale and helps you do even better work. But this cycle also operates in the other direction: if you’re not doing good work, that can demoralize you and make it even harder to. Since it matters so much for this cycle to be running in the right direction, it can be a good idea to switch to easier work when you’re stuck, just so you start to get something done.

士气通过工作复合：高昂的士气帮助你做好工作，这又提高你的士气，帮助你做得更好。但这个循环也在相反的方向运作：如果你没有做好工作，这可能会使你沮丧，使工作变得更加困难。由于这个循环朝正确方向运行如此重要，当你陷入困境时，转向更容易的工作可能是个好主意，这样你就能开始完成一些事情。

One of the biggest mistakes ambitious people make is to allow setbacks to destroy their morale all at once, like a balloon bursting. You can inoculate yourself against this by explicitly considering setbacks a part of your process. Solving hard problems always involves some backtracking.

雄心勃勃的人最大的错误之一是允许挫折一下子摧毁他们的士气，就像气球爆炸一样。你可以通过明确地将挫折视为你过程的一部分来为自己接种疫苗。解决困难问题总是涉及一些回溯。

Doing great work is a depth-first search whose root node is the desire to. So “If at first you don’t succeed, try, try again” isn’t quite right. It should be: If at first you don’t succeed, either try again, or backtrack and then try again.

做伟大的工作是一个深度优先搜索，其根节点是想要这样做的愿望。所以”如果第一次不成功，再试，再试”并不完全正确。应该是：如果第一次不成功，要么再试一次，要么回溯然后再试一次。

“Never give up” is also not quite right. Obviously there are times when it’s the right choice to eject. A more precise version would be: Never let setbacks panic you into backtracking more than you need to. Corollary: Never abandon the root node.

“永不放弃”也不完全正确。显然，有时候选择放弃是正确的。一个更精确的版本应该是：永远不要让挫折使你惊慌失措，以至于回溯得比需要的更多。推论：永远不要放弃根节点。

It’s not necessarily a bad sign if work is a struggle, any more than it’s a bad sign to be out of breath while running. It depends how fast you’re running. So learn to distinguish good pain from bad. Good pain is a sign of effort; bad pain is a sign of damage.

工作是一种挣扎并不一定是坏兆头，就像跑步时气喘吁吁并不一定是坏兆头一样。这取决于你跑得有多快。所以要学会区分好的痛苦和坏的痛苦。好的痛苦是努力的标志；坏的痛苦是损害的标志。

An audience is a critical component of morale. If you’re a scholar, your audience may be your peers; in the arts, it may be an audience in the traditional sense. Either way it doesn’t need to be big. The value of an audience doesn’t grow anything like linearly with its size. Which is bad news if you’re famous, but good news if you’re just starting out, because it means a small but dedicated audience can be enough to sustain you. If a handful of people genuinely love what you’re doing, that’s enough.

观众是士气的关键组成部分。如果你是一个学者，你的观众可能是你的同行；在艺术领域，它可能是传统意义上的观众。无论哪种方式，它都不需要很大。观众的价值并不会随着其规模的增加而线性增长。这对名人来说是坏消息，但对刚起步的人来说是好消息，因为这意味着一个小但忠诚的观众群就足以支持你。如果有几个人真心喜欢你所做的事，那就足够了。

To the extent you can, avoid letting intermediaries come between you and your audience. In some types of work this is inevitable, but it’s so liberating to escape it that you might be better off switching to an adjacent type if that will let you go direct.

在你能做到的范围内，避免让中间人介入你和你的观众之间。在某些类型的工作中，这是不可避免的，但摆脱它是如此解放，以至于如果转向相邻的类型能让你直接接触观众，你可能会更好。

²⁸The people you spend time with will also have a big effect on your morale. You’ll find there are some who increase your energy and others who decrease it, and the effect someone has is not always what you’d expect. Seek out the people who increase your energy and avoid those who decrease it. Though of course if there’s someone you need to take care of, that takes precedence.

你花时间相处的人也会对你的士气产生重大影响。你会发现有些人会增加你的能量，而其他人会减少它，而某个人产生的影响并不总是你所预期的。寻找那些能增加你能量的人，避开那些减少你能量的人。当然，如果有你需要照顾的人，那就优先考虑。

Don’t marry someone who doesn’t understand that you need to work, or sees your work as competition for your attention. If you’re ambitious, you need to work; it’s almost like a medical condition; so someone who won’t let you work either doesn’t understand you, or does and doesn’t care.

不要和不理解你需要工作，或者把你的工作视为争夺你注意力的竞争对手的人结婚。如果你有雄心壮志，你需要工作；这几乎就像一种医疗状况；所以不让你工作的人要么不理解你，要么理解但不在乎。

Ultimately morale is physical. You think with your body, so it’s important to take care of it. That means exercising regularly, eating and sleeping well, and avoiding the more dangerous kinds of drugs. Running and walking are particularly good forms of exercise because they’re good for thinking.

归根结底，士气是身体上的。你用身体思考，所以照顾好它很重要。这意味着要定期锻炼，好好吃饭和睡觉，避免更危险的药物。跑步和散步是特别好的锻炼形式，因为它们有利于思考。

²⁹ People who do great work are not necessarily happier than everyone else, but they’re happier than they’d be if they didn’t. In fact, if you’re smart and ambitious, it’s dangerous not to be productive. People who are smart and ambitious but don’t achieve much tend to become bitter.

做出伟大工作的人不一定比其他人更快乐，但他们比不做这些工作时更快乐。事实上，如果你聪明且有雄心壮志，不产出东西是危险的。聪明且有雄心壮志但没有多少成就的人往往会变得痛苦。

It’s ok to want to impress other people, but choose the right people. The opinion of people you respect is signal. Fame, which is the opinion of a much larger group you might or might not respect, just adds noise.

想给其他人留下深刻印象是可以的，但要选择正确的人。你尊重的人的意见是信号。名声，也就是你可能尊重也可能不尊重的更大群体的意见，只会增加噪音。

The prestige of a type of work is at best a trailing indicator and sometimes completely mistaken. If you do anything well enough, you’ll make it prestigious. So the question to ask about a type of work is not how much prestige it has, but how well it could be done.

一种工作的声望充其量是一个滞后指标，有时甚至完全错误。如果你把任何事情做得足够好，你就会使它变得有声望。所以关于一种工作要问的问题不是它有多少声望，而是它能做得多好。

Competition can be an effective motivator, but don’t let it choose the problem for you; don’t let yourself get drawn into chasing something just because others are. In fact, don’t let competitors make you do anything much more specific than work harder.

竞争可以是一个有效的激励因素，但不要让它为你选择问题；不要让自己被卷入追逐某事仅仅因为其他人在这么做。事实上，不要让竞争对手让你做任何比更努力工作更具体的事情。

Curiosity is the best guide. Your curiosity never lies, and it knows more than you do about what’s worth paying attention to.

好奇心是最好的向导。你的好奇心从不说谎，它比你更了解什么值得关注。

Notice how often that word has come up. If you asked an oracle the secret to doing great work and the oracle replied with a single word, my bet would be on “curiosity.”

注意这个词出现的频率。如果你问一个先知做出伟大工作的秘诀，而先知用一个词回答，我打赌会是”好奇心”。

That doesn’t translate directly to advice. It’s not enough just to be curious, and you can’t command curiosity anyway. But you can nurture it and let it drive you.

这并不直接转化为建议。仅仅好奇是不够的，而且你也无法命令好奇心。但你可以培养它，让它驱动你。

Curiosity is the key to all four steps in doing great work: it will choose the field for you, get you to the frontier, cause you to notice the gaps in it, and drive you to explore them. The whole process is a kind of dance with curiosity.

好奇心是做出伟大工作的四个步骤的关键：它会为你选择领域，带你到前沿，让你注意到其中的空白，并驱使你去探索它们。整个过程是一种与好奇心的舞蹈。

Believe it or not, I tried to make this essay as short as I could. But its length at least means it acts as a filter. If you made it this far, you must be interested in doing great work. And if so you’re already further along than you might realize, because the set of people willing to want to is small.

信不信由你，我尽量让这篇文章尽可能简短。但它的长度至少意味着它起到了一个过滤器的作用。如果你读到这里，你一定对做出伟大的工作感兴趣。如果是这样，你已经比你意识到的更进一步了，因为愿意想要做出伟大工作的人群是很小的。

The factors in doing great work are factors in the literal, mathematical sense, and they are: ability, interest, effort, and luck. Luck by definition you can’t do anything about, so we can ignore that. And we can assume effort, if you do in fact want to do great work. So the problem boils down to ability and interest. Can you find a kind of work where your ability and interest will combine to yield an explosion of new ideas?

做出伟大工作的因素是字面上、数学意义上的因素，它们是：能力、兴趣、努力和运气。根据定义，你对运气无能为力，所以我们可以忽略它。如果你确实想做出伟大的工作，我们可以假设你会付出努力。所以问题归结为能力和兴趣。你能找到一种工作，在那里你的能力和兴趣会结合起来，产生新想法的爆发吗？

Here there are grounds for optimism. There are so many different ways to do great work, and even more that are still undiscovered. Out of all those different types of work, the one you’re most suited for is probably a pretty close match. Probably a comically close match. It’s just a question of finding it, and how far into it your ability and interest can take you. And you can only answer that by trying.

这里有乐观的理由。有如此多不同的方式可以做出伟大的工作，还有更多尚未被发现的方式。在所有这些不同类型的工作中，你最适合的那个可能是一个相当接近的匹配。可能是一个滑稽地接近的匹配。这只是一个找到它的问题，以及你的能力和兴趣能把你带到多远。你只能通过尝试来回答这个问题。

Many more people could try to do great work than do. What holds them back is a combination of modesty and fear. It seems presumptuous to try to be Newton or Shakespeare. It also seems hard; surely if you tried something like that, you’d fail. Presumably the calculation is rarely explicit. Few people consciously decide not to try to do great work. But that’s what’s going on subconsciously; they shy away from the question.

比实际尝试的人多得多的人本可以尝试做出伟大的工作。阻碍他们的是谦逊和恐惧的结合。试图成为牛顿或莎士比亚似乎很自负。这也看起来很难；如果你尝试那样的事情，肯定会失败。可能这种计算很少是明确的。很少有人有意识地决定不尝试做出伟大的工作。但这就是在潜意识中发生的事情；他们回避这个问题。

So I’m going to pull a sneaky trick on you. Do you want to do great work, or not? Now you have to decide consciously. Sorry about that. I wouldn’t have done it to a general audience. But we already know you’re interested.

所以我要对你使用一个狡猾的技巧。你想做出伟大的工作，还是不想？现在你必须有意识地决定。对此我很抱歉。我不会对一般观众这么做。但我们已经知道你感兴趣了。

Don’t worry about being presumptuous. You don’t have to tell anyone. And if it’s too hard and you fail, so what? Lots of people have worse problems than that. In fact you’ll be lucky if it’s the worst problem you have.

不要担心自负。你不必告诉任何人。如果太难而你失败了，那又怎样？很多人有比这更糟糕的问题。事实上，如果这是你最糟糕的问题，你就很幸运了。

Yes, you’ll have to work hard. But again, lots of people have to work hard. And if you’re working on something you find very interesting, which you necessarily will if you’re on the right path, the work will probably feel less burdensome than a lot of your peers’.

是的，你必须努力工作。但再说一次，很多人都必须努力工作。如果你在做你觉得非常有趣的事情，如果你走在正确的道路上，你必然会这样，这份工作可能会比你许多同龄人的工作感觉负担更轻。

The discoveries are out there, waiting to be made. Why not by you?

发现就在那里，等待被发现。为什么不是你来发现呢？

Notes

The best lack all conviction, while the worst
Are full of passionate intensity.

Footnotes

1. 我不认为你可以给出一个精确的定义，说明什么是伟大的工作。做出伟大的工作意味着做某事如此之好，以至于你扩展了人们对可能性的认识。但重要性没有门槛。这是一个程度问题，通常在事情发生时很难判断。所以我宁愿人们专注于发展他们的兴趣，而不是担心它们是否重要。只要尝试做一些惊人的事情，并让后代来判断你是否成功。 ↩

2. 很多单口喜剧都是基于对日常生活中异常现象的观察。“你注意到没有…？“新想法来自于对这些非平凡事物进行这种观察。这可能有助于解释为什么人们对新想法的反应通常是前半部分在笑：哈！ ↩

3. That second qualifier is critical. If you’re excited about something most authorities discount, but you can’t give a more precise explanation than “they don’t get it,” then you’re starting to drift into the territory of cranks. ↩

4. Finding something to work on is not simply a matter of finding a match between the current version of you and a list of known problems. You’ll often have to coevolve with the problem. That’s why it can sometimes be so hard to figure out what to work on. The search space is huge. It’s the cartesian product of all possible types of work, both known and yet to be discovered, and all possible future versions of you.There’s no way you could search this whole space, so you have to rely on heuristics to generate promising paths through it and hope the best matches will be clustered. Which they will not always be; different types of work have been collected together as much by accidents of history as by the intrinsic similarities between them. ↩

5. There are many reasons curious people are more likely to do great work, but one of the more subtle is that, by casting a wide net, they’re more likely to find the right thing to work on in the first place. ↩

6. It can also be dangerous to make things for an audience you feel is less sophisticated than you, if that causes you to talk down to them. You can make a lot of money doing that, if you do it in a sufficiently cynical way, but it’s not the route to great work. Not that anyone using this m.o. would care. ↩

7. This idea I learned from Hardy’s A Mathematician’s Apology, which I recommend to anyone ambitious to do great work, in any field. ↩

8. Just as we overestimate what we can do in a day and underestimate what we can do over several years, we overestimate the damage done by procrastinating for a day and underestimate the damage done by procrastinating for several years. ↩

9. You can’t usually get paid for doing exactly what you want, especially early on. There are two options: get paid for doing work close to what you want and hope to push it closer, or get paid for doing something else entirely and do your own projects on the side. Both can work, but both have drawbacks: in the first approach your work is compromised by default, and in the second you have to fight to get time to do it. ↩

10. If you set your life up right, it will deliver the focus-relax cycle automatically. The perfect setup is an office you work in and that you walk to and from. ↩

11. There may be some very unworldly people who do great work without consciously trying to. If you want to expand this rule to cover that case, it becomes: Don’t try to be anything except the best. ↩

12. This gets more complicated in work like acting, where the goal is to adopt a fake persona. But even here it’s possible to be affected. Perhaps the rule in such fields should be to avoid unintentional affectation. ↩

13. It’s safe to have beliefs that you treat as unquestionable if and only if they’re also unfalsifiable. For example, it’s safe to have the principle that everyone should be treated equally under the law, because a sentence with a “should” in it isn’t really a statement about the world and is therefore hard to disprove. And if there’s no evidence that could disprove one of your principles, there can’t be any facts you’d need to ignore in order to preserve it. ↩

14. Affectation is easier to cure than intellectual dishonesty. Affectation is often a shortcoming of the young that burns off in time, while intellectual dishonesty is more of a character flaw. ↩

15. Obviously you don’t have to be working at the exact moment you have the idea, but you’ll probably have been working fairly recently. ↩

16. Some say psychoactive drugs have a similar effect. I’m skeptical, but also almost totally ignorant of their effects. ↩

17. For example you might give the nth most important topic (m-1)/m^n of your attention, for some m > 1. You couldn’t allocate your attention so precisely, of course, but this at least gives an idea of a reasonable distribution. ↩

18. The principles defining a religion have to be mistaken. Otherwise anyone might adopt them, and there would be nothing to distinguish the adherents of the religion from everyone else. ↩

19. It might be a good exercise to try writing down a list of questions you wondered about in your youth. You might find you’re now in a position to do something about some of them. ↩

20. The connection between originality and uncertainty causes a strange phenomenon: because the conventional-minded are more certain than the independent-minded, this tends to give them the upper hand in disputes, even though they’re generally stupider. ↩

21. Derived from Linus Pauling’s “If you want to have good ideas, you must have many ideas.” ↩

22. Attacking a project as a “toy” is similar to attacking a statement as “inappropriate.” It means that no more substantial criticism can be made to stick. ↩

23. One way to tell whether you’re wasting time is to ask if you’re producing or consuming. Writing computer games is less likely to be a waste of time than playing them, and playing games where you create something is less likely to be a waste of time than playing games where you don’t. ↩

24. Another related advantage is that if you haven’t said anything publicly yet, you won’t be biased toward evidence that supports your earlier conclusions. With sufficient integrity you could achieve eternal youth in this respect, but few manage to. For most people, having previously published opinions has an effect similar to ideology, just in quantity 1. ↩

25. In the early 1630s Daniel Mytens made a painting of Henrietta Maria handing a laurel wreath to Charles I. Van Dyck then painted his own version to show how much better he was. ↩

26. I’m being deliberately vague about what a place is. As of this writing, being in the same physical place has advantages that are hard to duplicate, but that could change. ↩

27. This is false when the work the other people have to do is very constrained, as with SETI@home or Bitcoin. It may be possible to expand the area in which it’s false by defining similarly restricted protocols with more freedom of action in the nodes. ↩

28. Corollary: Building something that enables people to go around intermediaries and engage directly with their audience is probably a good idea. ↩

29. It may be helpful always to walk or run the same route, because that frees attention for thinking. It feels that way to me, and there is some historical evidence for it.Thanks to Trevor Blackwell, Daniel Gackle, Pam Graham, Tom Howard, Patrick Hsu, Steve Huffman, Jessica Livingston, Henry Lloyd-Baker, Bob Metcalfe, Ben Miller, Robert Morris, Michael Nielsen, Courtenay Pipkin, Joris Poort, Mieke Roos, Rajat Suri, Harj Taggar, Garry Tan, and my younger son for suggestions and for reading drafts. | ↩