以下保罗·格雷厄姆博客《How to do great work》的英语原文和翻译，以及自己看后的想法及思考，这篇博客很长，我觉得在快餐文化的今天，很可贵，值得花费时间去细读，去领略其中的思想，接下来，开始吧：
原文与翻译①
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.
如果要汇总在任何领域做出伟大成就所需要的技能，它们的重合点会有哪些呢？我决定在实践过程中寻找这一问题的答案。
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.”
我本是想制作一个任何领域都能使用的行动指南。不过我也很好奇这些通往伟大成就的技能都是什么。于是在写出这份指南的同时我发现：这个技能列表是有确定答案的，而且它们并不是「努力」一词就能概括的。
The following recipe assumes you’re very ambitious.
以下的秘诀假定你有非常高的抱负（追求卓越）。
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，是决定伟大的事具体是做什么。这件伟大的事需要具备以下三个特质：你在这件事上有天赋、你对这件事有强烈兴趣、以及你在这里有施展才华的空间。
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. [1]
在现实生活中，你基本无需担心第三点，有野心的人对平台的挑选已经足够保守了。所以你主要需要考量的，就是自己的天赋和兴趣。[1]
[1] I don’t think you could give a precise definition of what counts as great work. Doing great work means doing something important so well that you expand people’s ideas of what’s possible. But there’s no threshold for importance. It’s a matter of degree, and often hard to judge at the time anyway. So I’d rather people focused on developing their interests rather than worrying about whether they’re important or not. Just try to do something amazing, and leave it to future generations to say if you succeeded.
[1] 我认为我们无法对「伟大的事」下一个精确的定义。伟业意味着将某件重要的事情做得极为出色，拓展了人们对于可能性的认知。但「重要」是没有标准的，它只是一个程度问题，而且往往很难在当时做出判断。所以，在我看来，比起衡量自己做的事情是否重要，更应该做的是专注发展自己的兴趣与爱好。只要尝试去做了不起的事情，未来的人们自会评判你是否成功。
That 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.
这两件事听起来简单，找起来难。当你年轻的时候你并不知道自己究竟擅长什么，其他工作又在做什么，有些你最终会做的事情也许现在还不存在呢。所以，就算有些人在 14 岁就知道自己想做什么，大部分人都需要不断寻找自己的目标。
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.
而寻找目标的方法，就是去实践。如果你不知道从哪开始实践，那就先猜一个吧。更重要的是动起来。你会偶尔猜错方向，但没有关系。了解不同的事情总是好的，有些最最重大的发现正来自于对不同领域的链接。
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.
养成创作你个人项目的习惯。简单来说，就是找到你想要做的事。不要让别人左右你对于「工作」或者「事业」的定义。如果有一天你做成了伟大的事业，那大概率做的是你自己的项目。虽然它可能隶属于某个更大的事业版图，但你是这部分成果的核心驱动力。
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.
那什么能成为你的个人项目呢？答案是任何让你热血沸腾的事。随着年龄的增长，和你对事物审美判断的演变，令你兴奋的事物和重要的事物逐渐会产生交集。 7 岁的时候做一个巨大的乐高模型让你热血沸腾， 14 岁时自学微积分让你热血沸腾， 21 岁时关注那些没有定论的物理问题让你热血沸腾。这些事情会变化，但是不变的是那份真正兴奋悸动的心情。
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.
这份兴奋衍生出的好奇，既是伟大事业的发动机又是它的方向舵。它不光为你提供动力，还为你指明方向。当你认真倾听的时候，就能听到是什么事在召唤你而来。
What are you excessively curious about — curious to a degree that would bore most other people? That’s what you’re looking for.
什么是就算他人觉得无聊透顶你也无法抑制好奇的事情？那就是你要做的伟大的事。
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.
当你发现了自己非常好奇的事情以后，下一步就是去学习足够带你去到行业顶尖的知识了。知识是慢慢积累的，也许从远处看你具备的知识已经填出了完美的弧线，但是当你学到足够的知识去近距离观察，就会发现那中间的缝隙了。
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. [2]
那么下一步就是去观察这些缝隙。这时会需要一些技巧，毕竟我们的大脑总是习惯于忽视这些缝隙，并欺骗自己去为世界建一个更简单的认知模型。但是，很多发现都是从问出别人觉得理所当然的事中诞生的。[2]
[2] A lot of standup comedy is based on noticing anomalies in everyday life. “Did you ever notice…?” New ideas come from doing this about nontrivial things. Which may help explain why people’s reaction to a new idea is often the first half of laughing: Ha!
[2] 很多单口喜剧的创作都是来自对日常生活中反常现象的观察：「你有没有注意到……？」 而新想法往往来自对并不琐碎事物的观察。或许，这可以解释为什么人们对新想法的反应像笑出声的前半部分一样会来一句：哈！
If 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.
如果你得到的答案看起来很怪，那就更好了。伟大的事情总是带着特立独行的标签。无论是数学还是艺术，我们都能发现这个特点。如果这份独特确实出现了，建议你拥抱它，而不是尝试改变它。
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. [3]
勇敢地去追寻特立独行的想法，就算其他人对这个话题不怎么感冒。事实上，他人的不感兴趣是个更好的信号。如果你关心的是一个别人忽视的问题，而且你的专业程度足够让你相信自己的判断，那这就是你最好的选择。[3]
[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.
[3] 第二个限定条件至关重要。如果你对某件大多数权威人士不看好的事情感到兴奋，但你无法给出比 「他们不懂」 更精确的解释。那么，你就跑了题开始进入怪人的领域了。
Four 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.
总结一下，寻找你的个人项目有四步：选择一个领域、学习足够到达前沿的东西、发现缝隙、探索其中有前景的。这就是所有做伟大的事情的人所做的事，从绘制者成长为实践者。
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.
第二和第四步需要你投入大量时间和精力。的确，我们努力付出不代表就能成就伟业，但是从大量经验来看，不付出确实成不了事儿。而不断投入的前提是你自身的兴趣。兴趣与好奇会比保持勤奋的习惯更能驱使你前进。
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.
好奇心、愉悦感和做成伟业的欲望，是三个最强大的动力源泉。有时，他们三者会逐渐趋同，而最强的驱动力正来自于三者的结合。
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.
终极大奖就是寻找到缝隙中那根有可能生长出来的枝杈。你发现了知识表层的裂缝，将它破开，而后洞见了一个崭新的世界。
第一段感想
说起来，很感慨，我曾经很多的困惑，就被硅谷教父这一段高度概括了，有醍醐灌顶之感，很多年教育，遇到过很多老师，但没有一个老师跟我说过这样的话，只是说兴趣是最好的老师，但兴趣是什么呢？甚至很多老师根本不会理会你的兴趣，你只需要完成对应课业就可以了，兴趣是什么？比得上升学率吗？
对于一名普通人来说，高考是改变人生的机会，可是据我了解，也仅限于我所知所想，选学校，选专业，参考的都是学校排名，专业排名等等，极少考虑兴趣，写到这里，才发现，原来前提是“The following recipe assumes you’re very ambitious.”。
确实，如果只是需要平凡稳定的生活，并不需要这些，只需要按部就班即可，这就会引申出另一个问题：“为什么要追求卓越？”
这就是一种社会默认的限定，你这么平凡，一点天赋都没有，你这是异想天开，你就该老老实实的平凡，等等，好像追求卓越是一种僭越，下面也有讨论，暂且不展开，总之，对于普通人，开局好像就要求就该平凡到底，兴趣，像是你不该奢望的东西。
好了，当你跨越这些， 接下来就是上面所说的路途了，找到兴趣所想，找不到，就去实践，去猜，是那么是别人觉得无聊透顶但自己觉得很有趣的事，什么是自己可以不断重复而不厌烦，熟练到别人觉得你有天赋的事情，也许就是你的兴趣所向，应该朝着这个方向去前行，争取做出卓越之事。
其中说到很多细节，首先是知识的积累，然后是观察，只有兴趣才会带来观察，只有知识的积累才能带来认知，不断的观察，才会有想法不断的展现，才会有机会去找到那个缝隙吧？
“So while some people know what they want to do at 14, most have to figure it out.”，有人14岁就知道自己的方向了，大部分人则需要不断的去寻找，正常来说，我们都会落在大部分人这里，在繁复的生活中，去寻找自己的方向和兴趣，如果找到了，一定要抓住机会，去追求卓越。
以上第一段感想。
原文与翻译②
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. [4]
让我们再聊聊「寻找个人项目」这个复杂的话题，如何找到自己想要做的事情。它的难点在于，除非真正去做，你根本无法判断这些事到底是怎样的。这意味着你可能需要在某一行业工作数年才能知道自己究竟是否爱好和擅长。而同时，你又没有机会同时去体验或学习大部分其他行业。那么最差的情况是，你会因信息不全面而有些晚地开始真正属于你的事。[4]
[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.
[4] 寻找要着手解决的问题并不仅仅是在当前的你和已知的问题之间寻求匹配。你通常需要与问题共同演化。这就是为什么有时候我们很难确定要做什么。搜索空间是巨大的。它有将所有可能类型的工作（包含已知，也包含尚未发现的）与你未来的所有可能一一相乘后再求和，那么多种可能性。
因此你不可能搜索完整个空间，你必须依靠启发式的方法来生成有希望的路径，将最佳的匹配都聚在一起。不过这个过程并不总会是自然流畅的：不同类型的工作之间的相似性并非完全由历史的偶然性决定，也有其内在的差异。
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.
野心的本质会恶化这个问题。野心有两种，一种是在你找到兴趣点之前就有的，另一种由你的兴趣产生的。大部分做出伟业之人的野心，是这两种形式的结合。如果你在找到兴趣点之前就十分雄心勃勃，那你往往会更难找到自己想要做的事情。
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.
大部分国家的教育体制将「找到自己想做的事」包装得很简单。他们期望你在知道自己真正喜欢什么之前长期投入一个领域。而结果就是，一个有野心的人常常被教育系统当做一个破坏者。
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.
他们不愿意承认，现有的教育系统无法帮你找到自己想做的事，而且这个系统还假设你能在青少年时期就魔法般猜中自己未来的事业。既然他们不愿意承认，那么我来说明真相吧：在这条寻找道路上，你只能依靠你自己。有些走运的人能一下子猜中，但是余下的会跟大部分人一起，在很多条路中间磕磕绊绊、反复研究。
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. [5]
所以当你年轻且有野心，却不知从哪下手时，该怎么办呢？首先，你不应该随波逐流，以为答案会从天而降，你需要行动起来。这世上并没有一本能为你剥茧抽丝的说明书，我相信这一点在你阅读那些伟人自传时就该意识到了。在寻找要探索的事业时，运气占比是非常大的。那些伟人总是在偶遇贵人或偶遇好书后，灵光一闪，就找到了要做的伟业。所以，你要做的，就是增加自己被运气青睐的概率。而增加的方式，正是保持好奇心。尝试更多事、见更多人、读更多书、问更多问题。[5]
[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.
[5] 好奇心强的人更有可能完成伟大工作，这一特点有很多理由可以解释。其中一个最微妙的原因是，通过广泛撒网，他们更有可能尽快找到正确的工作。
When 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.
当你有疑虑的时候，将一切围绕着自己的兴趣去优化。一个领域会随着你对它的了解而逐渐变化。比如说，数学真正在研究的事情和你从高中数学课学到的相差甚远，所以你需要从不同角度和不同层面更全面地去了解这些事物。但是你要注意，如果一个领域没有随着你的深入了解而变得越来越有趣，那么你该停下来了，那不是你要做的事。
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.
不要担心你的兴趣点是否和他人不同。你的品味越独特越好。独一无二的品味往往是强烈的，而这份强烈意味着你将更加高产。同时，你在更少人开拓过的疆土上更容易发现新的东西。
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.
找到一个真正适合你的事的标志就是，你甚至觉得在别人看来复杂而可怕的东西是那么的可爱。
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.
不过领域和人类不同，你不需要对它保持忠诚。如果在你探索的过程中发现了更让你兴奋的东西，不要害怕改变。
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.
如果你是在为他人提供什么，请在那之前先确认你提供的东西是他们确实需要的。做到这一点的最好方法就是做连你自己都想要的东西，写你会想读的故事、造你会想用的工具。同时，因为你身边的人大概有类似的诉求，他们将会成为你的首批观众。
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. [6]
为他人提供什么一样需要遵循兴趣原则。很明显，最让人想读的故事是你想读的故事。我反复把这一点单拎出来说是因为很多人思考这件事情的时候都是错误的。他们不去做自己想要的，而是做一些幻想出的、所谓比他们自己更成熟的观众所需要的。而只要你这样思考，就一去不复返了。[6]
[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.
[6] 如果你觉得观众不如你精明，带着这种态度为他们制作产品也可能是危险的，因为你和他们说话的语气很可能会显得高高在上。如果你以愤世嫉俗的方式做这件事，你或许可以赚很多钱，但这不是通往伟大工作的道路。不过说回来了，这些人大概并不在乎。
There 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.
当你试图去发现自己要做的事情时，世上会出现各种把你带偏的力量：肤浅、潮流、恐惧、金钱、政治、他人的愿望、有影响力的骗子等等。可是如果你偏离了自己真正的兴趣，你将沦为被这些力量支配的玩物。但如果你坚定自己的兴趣，你就不会偏离轨道。
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.
跟随你的兴趣听起来有些被动消极，但如果你真的实践这条原则，这意味着你需要跟随自己的兴趣克服一个又一个难关。你经常需要面对拒绝和失败，而这需要极大的勇气。
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.
虽然面对拒绝和失败需要勇气，但这不意味着你要事先进行周全的计划或准备。在很多时候，完成伟大工作其实很简单：在让你热血沸腾、又能激起你野心的事情上投入大量精力，一些好东西就会自然诞生。你不需要做一个计划而后按部就班地完成，你只是找到不变的东西，而后顺你所想尽你所能。
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，它只能为你可以想象的成就带来帮助。你可以在小时候就决定有一天赢得金牌或发家致富，但是你无法计划出这过程中的优胜劣汰。
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.
我认为对大部分想做出伟业的人来说，正确的对策就是不要做太多规划。在每个阶段都去做看起来最有趣、且能在未来给你提供最好选项的事。这也可以说成是，一直「迎风而上（Stay Upwind）」。从经验看来，大部分做成伟业的人都是这样做的。
第二段感想
保持好奇心去寻找，不惧试错成本
这一段也是在讨论，如何找到自己感兴趣想做的，并且是值得去做的事情，并把事情做成卓越的事业。因为教育系统的原因，我们很多时候都是被迫选了一个方向，这其实跟作者的建议也差不多，就是猜，但很大的区别是，很多人可能就随着这个方向走下去了，也许从来也没有问过，这是否是自己感兴趣的事情。作者的建议本是去尝试，去猜，而不是一成不变，虽然对于作者来说，如果遇到不适合自己的方向，转而去寻找其他方向，是很自然的事情，但就我面临的生活来看，并不太相同。
中国古话说:“男怕入错行，女怕嫁错郎”，跟作者想法有点不同，更强调了试错成本，很多时候，并没有太多的选择机会，哪怕你知道这不是你感兴趣的工作，但你毕业于这个专业，从事了这个行业，就像是一种羁绊，能保持好奇心去探索，并在遇到真正喜欢的事业时，有挣脱这份羁绊的勇气的人，也是少数。
更不用说，社会规约给你定下的路线，学习，毕业工作，成家立业（我认为这里的立业跟作者所说的事业不是一个东西，我认为这只是我们文化体系下，立业仅表示你经济独立了），养儿育女，仿佛就像一条生产线，推着你前行，至于你的兴趣，所谓追求卓越事业，都会被埋葬在这里。
所以作者也说了，会有很多其他的力量把你带偏，更加强调了定下你兴趣和方向的东西的重要性，一旦找到，应该是坚定不移的，如果动摇了，说明你还没找到，需要继续找，只是不能失去去寻找的动力，保持你的好奇心。
区分野心与兴趣方向
在这里之前，作者也说到了有两种情况，一种是先找到自己的兴趣和方向，然后有追求卓越的野心，另一种是先有野心，然后才找到兴趣和方向，作者认为大部分能成功的人，是两种情况的结合，第二种会更难找到自己真正感兴趣的事情。我的理解是，如果“找到兴趣点之前就十分雄心勃勃”，那将会走向其他的方向，举个例子，在压力很大的现代社会，大家都在追求财富自由，追求金钱，这也可以说是一种野心，但是这种野心会被困在如何赚很多很多的钱的漩涡里，可能有人能成功，然后利用财富去寻找自己的兴趣和方向，但终究是少数吧？甚至把积攒财富变成自己兴趣和方向了？
我觉得目前，大部分人找寻的路线都是第二种，先让自己野心勃勃，获取财富之后，才去寻找自己的兴趣和方向，我不知道正确与否，我也正走在路上。只不过作者给出的是另一条不同的路线，直接走在寻找兴趣和方向的路上，并实现自己的野心，成就卓越。
然后作者再次强调了，如果一个东西，大部分人都觉得复杂而可怕，但你觉得有趣，那就有可能是你要追求的，真正适合你的事。同样也说不需要对事业保持忠诚，有更加感兴趣的事，就去追求，说到底，找到真正适合自己的事是很难的，有可能永远找不到，找到了，也需要坚持，坚持了，还需要面对拒绝和失败….
没有百分百秘诀，只有依靠自身
我很感激作者的真诚，他没有像其他成功学那样：跟着我学，买我的书，就一定可以成功！也没有像教育系统那样：只要努力，你就一定能成功！作者一直在强调，这不是一件百分百成功的事，“这世上并没有一本能为你剥茧抽丝的说明书”，那作者想表述什么呢？他只是分享了他的想法和经历，并告诉我们，如何做，能增加做成一件卓越的事的概率，是的，仅仅事增加概率，运气仍是很大的一部分。
而且，我认为，能找到自己真正适合并热爱的事，也是很满足的一件事，哪怕做不成卓越的事，起码方向是正确的。
所以，落到实处，我们需要尝试更多事、见更多人、读更多书、问更多问题。
做自己都想要的产品（服务），并果断行动
其中作者还谈到在实际的实践中，细节上，如何将事情做得卓越，我理解，也可以说是，怎么样将事情，或者工作，或者产品，做得最好？那就是做出你自己想要得东西，做你自己想要产品，制作你自己想吃得美食，为什么这么说？在实际的工作中，因为之前的分配模式下，大部分人都不会从事自己喜欢的工作和生活，所以他们并不关注自己生产和提供的服务，自己设计的产品，自己都不会愿意去使用，自己提供的服务自己都觉得不好，这怎么可能成就卓越呢？哪怕可以暂时的盈利，我认为也是不长久的，因为这是你自己都不会想要的东西，怎么奢望别人会喜欢呢？怎么产生价值呢？如果你认为的用户和观众不如你聪明，可以愚弄用户和观众，作者也解释了，也许你可以赚到钱，但这不是通往卓越的路。我也认为，愚弄可以一时，但终将会有反噬。
最后作者建议做决策时，不应该做太多的规划和计划，不然就会是太多的空想和消耗精力，有时候，想太多的规划，开再多的会，并不会让事情更加容易，反而会降低效率，因为变化是一直存在的，不可能全部都能规划到，只有找到适合的兴趣和方向，也许那就是作者说的不变的东西。
原文与翻译③
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.
即使你找到了想去做的事情，做起来并没那么简单。有时候，你一睁眼就会有新想法，恨不得立刻去上班，但更多的时间，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.
灵感并不会自然而然地带你前进。这一路上会出现逆风、洋流和隐藏的浅滩。所以，正如在海上航行一样，做事也自有一套技巧。
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.
举个例子，虽然你应该努力投入精力，但是你也有可能用力过猛，你要是这么做，会发现边际收益越来越少：过度疲劳使人愚钝，最终还可能有损健康。而做事的边际收益取决于你做什么事。有些事就是很难，你一天最多只能做四五个小时。
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，投入的时间应是连贯的。尽量成块地安排你的时间，把一整块倾注到这件事上。如果你知道可能会被打断，你会回避艰难的任务。
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.
万事开头难，开始可能比坚持还难。有时候，你得靠「自我欺骗」才能跨过那第一条鸿沟。不过别担心，这是自然现象，并不是你的错。
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.
无论是开启一天，还是开启一个项目，你都需要一定能量才能启动。既然「开始」比「坚持」需要更多能量，那不如小小欺骗自己一下说：这两者需要的能量其实差不多。
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.
大部分时候，自我欺骗在做成大事的路上都是错误的，不过，这是例外。当我在早上因为犯懒而不想工作时，我会骗自己：「我就检查检查目前为止的进度吧。」五分钟后，我就会发现自己的错误，或需要补充的地方，自然就开始做事了。
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?”
同样的自我欺骗，还可以用于开启一个新项目。欺骗自己，跟一个项目实际需要的工作量，其实没多大关系。很多伟大的成就都是从一句「这事儿能有多难」开始的。
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.
这也关联到年轻人有优势的一点。他们更加乐观，尽管他们的乐观主要源自无知，但在这种情况下，无知有时能战胜渊博。
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.
试着完成自己开启的事情，即使它比你预想的要更费劲。完成一件事，不光是一场关于自律的修行。很多项目的高光时刻就发生在收尾阶段。
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. [7]
另外一个可以撒的谎，是夸大你所从事的工作的重要性，至少对自己这么撒谎。而如果这件事能给你带来新的发现，那它就不算是谎言了。[7]
[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.
[7] 这个想法我是从哈代的《一个数学家的辩白》中学到的，我推荐给任何有雄心壮志在任何领域做出伟大工作的人。
Since 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. [8]
既然开始做事可以按天或按项目来看，它们也各自对应了一种拖延方式。拖延项目是更加危险的。你把自己想要开启一个项目的野心年复一年地拖下去，只是因为现在时机不太对。而当你按年来拖延的时候，你将积攒越来越多未做成的事。[8]
[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.
[8] 就像我们高估自己一天能做的事情和低估自己在几年内做的事情一样，我们往往也高估了拖延一天造成的损害和低估了拖延几年造成的损害。
One 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.
项目拖延更危险的理由之一，就是这种拖延会把自己伪装成你要做的工作。你没有游手好闲，但是你在勤奋地做另一件内耗自己的事。所以对项目的拖延不像对一天的拖延那样能迅速引起你的警惕。你太忙了，以至于没有注意到这份拖延。
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. [9]
打败项目拖延的方式就是偶尔停下来，问问自己：「我是在做我最想做的事吗？」当你年轻时，这个答案可以是「并没有」，但是年龄越大，这个否定的答案就会越危险。[9]
[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.
[9] 通常情况下，你不能仅仅做自己想做的事情就能得到报酬，尤其是在初期阶段。这时你有两种选择：做与你想做的工作相近的事并逐渐接近目标，或者完全做其他事并在业余时间进行自己的项目。这两种方式都可行，但都有缺点：在第一种方式中，你在工作中的所求会受到限制；而在第二种方式中，你必须努力争取时间来做自己的项目。
Great 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.
做成伟业，一般意味着花费一段在他人看来长到离谱的时间。但是，你不能把这段时间看成是一种成本，否则你会因巨大的成本而被劝退。你必须找到能让你充分参与的工作。
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.
也许在做某些事情的时候，你得先忍受数年、努力工作才能谈收获，但伟大的事业并非如此。伟大的事会因为你持续关注一件你真心感兴趣的事而实现。这样当你停下来回望时，你会讶于自己竟已走过了那么长一段路。
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.
我们讶异的原因在于我们会低估工作的累积效果。一天一页的工作量听起来不多，但是这样连续一年你就能写成一本书了。持续去做，这就是关键。做成伟业的人并不是一天就做完了多少件事，而是至少会做完某件事，不是无所事事。
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.
如果你做的事能够累积，那么你就会收获指数级的成长。大部分人并没有意识到这一点，不过指数级成长值得我们停下来想一想。例如学习就符合这个现象。你学得越多就学起来越轻松。积累用户是另一个例子，你有越多的粉丝，就会有他们带来的更多新粉丝。
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.
指数增长的问题是，在一开始的时候它只有一个平缓的坡。它虽让我们感觉平缓，却依旧是一个指数级别的增长。不过因为我们无法一上来就直观感受到，所以很容易在指数增长的初期低估它。
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.
一些能够指数增长的东西具有着超高价值，而它们也值得你花更多精力去启动。不过因为人们常在初期低估指数增长，所以这些启动一般都是无意间的。人们扛过初期这段学习很多新事物却没有回报的阶段，只是因为从经验上他们知道学习新东西就是要一个助推，或是他们只能一个粉丝一个粉丝积累而别无他法。如果所有人都清醒地知道如何投资指数增长，那就会有更多人做这件事了。
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.
事业不是你一股脑地努力就能做成的。当你散步、沐浴或是躺在床上的时候，那种间接的思考是更有力量的。让你的思绪飘一会儿，你往往就能解决正面对抗无法解开的问题了。
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. [10]
不过你仍需要保持传统意义上的努力来从这种间接思考中获益。你不能只是四处游荡做白日梦。这种遐想需要植入到刻意工作中才能获得养料。[10]
[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.
[10] 如果你安排好你的生活，它会自动带来专注和放松的循环。一个完美的安排如同一间你能安心工作并且可以步行往返的办公室。
Everyone 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.)
每个人都知道在做事的时候应避免分心，不过在思绪中徜徉时也应该避免分心。这样当你放飞思绪的时候，它才会飞向你在当下最关心的问题。所以我们真正要避免的，其实是将你要做的事推下第一优先级的那种分心，否则你就会将这种自由思考浪费在走神中了。（例外：不要避开让你分心的爱）
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.
有意识地多了解你所在领域的作品，并以此来培养自己的品味。毕竟，在你知道什么是最好的、以及成为「最好」需要做什么之前，你也许不知道自己准确的目标。
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. [11]
不过成为最好就可以是你的目标。如果你不是想着怎样做到最好，你甚至都无法把事情做到优秀。这个事实已经被各种领域证实了，而我猜测这原理背后的原因，可能是做好的野心自然会导向眼高手低的结果；或想做成最好的野心本质上与仅是想做好的野心不同；又或者「做好」的标准太过模糊了，导致最好的想法比只是做好的想法更驱动人。其实以上这三点原因，大概都是对的。[11]
[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.
[11] 可能有一些没有野心的人在不知不觉间做出了伟大的工作。如果我们试图拓展之前的规则来涵盖这种情况，那就是：除了做到最好，也不要给自己留任何后路。
Fortunately 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，「做最好」的目标被大量实践证实确实有用。虽然「做到最好」听起来给了自己太重的包袱，但在现实中，你往往会因为目标为「最好」而比别人多想几步。这个优势让人兴奋，也给人有一种莫名的松弛感。「做到最好」让事情简化：毕竟从某种意义上来讲，「做到最好」比「做好」更直观。
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.
而设立「做到最好」这样的高目标，就相当于去思考人类在未来 100 年会关心什么。这并不是因为别人的想法比你自己的重要，而是因为 100 年后依旧被需要的东西，大概率才是真正的好东西。
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.
不要过多尝试改变做事风格。就去做到你能做到的最好就行了，再独特的风格也无法帮助你达到最好。
Style is doing things in a distinctive way without trying to. Trying to is affectation.
风格是自然而然产生的、属于自己的工作模式。刻意做出风格会显得矫揉造作。
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. [12]
做作的本质是装作另一个不是自己的人去做事。你会置身于一个有魅力但是虚假的人设里，而当你因为这份魅力沾沾自喜时，这份虚假也会在你的事业中尽数体现。[12]
[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.
[12] 像演戏这样的工作中，情况会变得更加复杂，因为其目标是扮演一个虚假的角色。但即使在这种情况下，也有可能受到影响而过于做作。也许在这些领域中，应该避免无意识的做作。
The 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.
成为他人对年轻人来说是最大的诱惑。他们经常感到自己谁都不是。但是你不需要担心这个问题，因为只要做足够有野心的项目，这个问题就迎刃而解了。你不是路人甲，你是能做成伟业的人。所以去做吧，做事风格什么的自然会到来。
“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」是非常有用的一项原则，但是我们如何用正向语言叙述它呢？怎么能说「要做…」而不是「不要做…」？最好的答案是「保持真诚」。如果你是真诚的，那么你能避免掉做作以及和它类似的一系列阻止你成为最好的绊脚石。
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?
保持真诚的核心是保证学术诚实。我们教给孩子们诚实是一个不自私的美德，它是一种牺牲。但其实诚实也是一种力量。想拥有新的灵感，你就得有一双发掘真相的慧眼。你在尝试比别人看到更多的真相。而如果你无法保持学术诚实，又如何拥有发觉真相的慧眼呢？
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. [13]
一个避免学术不诚实的方法就是对相反观点持有更乐观的态度。积极主动愿意承认自己的错误。当你承认在某件事上的错误后，你就自由了。而在那之前，你需要承受因不愿承认而有的重量。[13]
[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.
[13] 只有当你的信念是不可质疑且不可证伪的时候，才能放心地拥有它们。例如，拥有「法律面前人人应平等」的原则是安全的，因为带有「应该」这个词的句子并不是对世界的陈述，因此很难被证伪。如果没有证据能够证伪你的原则，那么你就不需要为了维护自己的原则去忽视部分现实。
Another 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.
除了学术诚实，真诚的另一个更细小的构成因素是保持轻松，不拘小节。不拘小节比它的反义词一板一眼重要了很多。它不光意味着去掉程式化的东西，删繁就简，也意味着关注真正重要的东西。
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.
过度程式化和矫揉造作有一个共同点，就是你在尝试「看起来如何」，而并非真正「做出来如何」。这就是为什么世俗意义上的书呆子在做出伟业上有优势：他们不在「看起来好」上下太多功夫。事实上，这也正是书呆子的定义。
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.
书呆子有一种单纯的勇敢，而这正是做出伟业所需要的。这无法习得，而是从小保持的。所以保持住。做那个把想法说出去的人，而不是做靠在椅背上说出貌似有深度批评的人。「说起来简单做起来难」是真的，通往伟大事业的路途从不简单。
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.
可能对于一些职业来说，愤世嫉俗和消极是一种优势，但是如果你想做成伟大的事，就算看起来有点傻气，乐观积极也是你的优势。反其道而行之是我们都熟悉的老话了。旧约中说，以免自己看起来像个傻瓜，你最好还是保持安静。但是这个意见是为了让你看上去聪明。如果你真的想发现新的事物，那么最好冒险把你的想法说出口，告诉别人。
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. [14]
有些人天生真诚，而有些人则需要付出努力。无论哪种真诚都是足够的。但对于认为不真诚就能做出伟大的事的观点，我保持怀疑态度。连拥有真诚去做成伟业都很难了，何况连真诚都没有呢？你没有足够的试错空间去容纳因学术不诚实、教条死板、和为了看起来潮流酷炫而造成的扭曲。[14]
[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.
[14] 矫揉造作比学术不诚实更容易纠正。矫揉造作通常是年轻人的缺点，但它随着时间的推移会逐渐消失，而学术不诚实更多是一种性格缺陷。
第三段感想
万事开头难，但应该及时开始
这也是我觉得很困难的一个问题，有想法，或一些需要的工作后，开始需要的能量好像远远大于项目本身，看来有必要依靠一下“自我欺骗”，比如起床时，只是起来上个厕所，就不会再睡懒觉了，只是检查一下进度，就可以进入工作了。并且，不单单是从大的计划或工作来说，开始很难但应该尽早去开启，其实生活中，或者日常的工作等，有很多琐碎的事情，也是因为难于开始，才导致很多拖延。
日常中，很多我们推后的事情，经常就是会直接放弃了，那是否可以，在重要的事情上，我们不管规划如何，先开个头呢，也许会是一个好的方法。
偶尔停下思考
这个在工作一段时间后，比较有感触，在公司安排好的排期中，你会发现时间过得很快，很容易就沉浸在忙碌中，也会慢慢失去自己的方向。如果从事的职业不是自己相关兴趣的，情况可能更为明显。
所以，还是应该主动找出时间，去思考，“我是在做我最想做的事吗？”，并尽可能的去修正，每年一次的总结，也许是不错的方法。也可以通过这样，去避免拖延。
积累与指数级效应
也许是快餐文化的影响，做什么东西总是想着速成，想着很快搞好，却忽略积累的力量，以及很多伟大的事迹都是要一步一步积累的。我觉得所谓复利，和指数增长，大家都看过很多，为何在应用的时候，又显得这么难呢？坚持是一个很大的原因，同时也需要耐心，耐得住寂寞和初期的缓坡，急于求成，是没办法坚持的，这与上面说的，要找到自己兴趣所向，又是相呼应的，因为是自己兴趣所向，就不存在耐心的问题了，每一点滴的进步都会是欣喜的。
这可能才是指数增长的秘密吧，你需要坚定的兴趣。毫无犹豫的开始，耐心的坚持，才有指数的机会吧？
想着做最好
我记得解数学题的时候，总是会有隐含的条件藏在题目中 ，我觉得，想着做最好，也是如此，这里隐含了一个前提，你会去思考，想要做最好的东西，绝大部分人来说，做一个东西，做完了就是完成了，只有很少才会去思考，这个东西还有没有优化的空间？还可以不可以做更好，以至于做到最好？
只要你去想了，你会发现其实很多东西并不是最好的，也许你没想全面，也有可能是真的不完美，但我更觉得重要的是，我们去思考的这个过程。
而且其中有想法的人，也会遇到很多情况，就比如说，提出自己的想法，会被嘲笑，提出的想法，害怕被人取笑，觉得存在就是合理，自己不应该做出头鸟等等，困难和问题总是多的，只能说，在有选择的情况下，如果要追求卓越的事业，想要发现有趣的新事物，“那么最好冒险把你的想法说出口，告诉别人。”
同时保持真诚，而不是去塑造人设，塑造虚假的形象，我觉得会这么做的人，跟第二段所说的，认为自己比其他人（用户）聪明，通过欺骗来达到目的的人，本质上是一样的，可能会变得富有， 但不会成就卓越。
同时飘着思考也是很有意思的体验，当你关注于自己的问题时，有时候飘着思考，反而更容易找到答案。
以上第三段的感想。
原文与翻译④
Great 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.
伟业不光和制造者保持一致，也有它自己不变的调性。制造者与被制造的事物是一体的。所以当你在做事时面对一个选择，选那个能让一切保持一致的。
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?
有时，你可能需要扔掉一些东西并重新来过。虽然这不是必须的，但是当你真正需要的时候，你得愿意放开手。学会放手是需要努力的。当你有需要从头来过的东西时，对现状的偏见和自身的惰性会一同让你否定这个现实。而想要战胜偏见和懒惰，就要问自己：如果我已经做出了改变，是否还愿意回到现在的状态？
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.
你要有信心、大胆地去做取舍。不要保留一些不合适的东西，即使它们让你感到骄傲，因为留下它们只会慢慢消耗你自己。
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.
诚然，在有些事情中，将任何你做的事情都联系在一起是好的。这个结果会更加集中，而你也可以更好地理解自己在做的事。但是当你需要舍弃的时候，也不需要通过自我欺骗，来硬说这里有实打实能留下来的东西。
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.
数学的优雅也许听起来像从艺术那里挪用来的比喻。当我第一次听到「优雅」一词用来形容一个数学证明的时候，我也是这么想的。但是现在，我理解到艺术优雅的主要成分就来源于数学的优雅。而优雅与否是一个远比数学本身更有用的标准。
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.
保持优雅的背后是日复一日的长线投资。费力发现的解决方法常在短期内更被重视。你所付出的努力和问题本身的复杂能够给人留下印象，但这只是暂时的。
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.
一些最伟大而优雅的作品或许看起来只费了一点点力，这是因为从某种意义上它们经过了千万次积累，已经在那了。它们不需要被建造，只需要被发现。当你很难评价这个东西是发明还是发现之时，这是伟业将要发生的好苗头。
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.
当你做的事可以既被看作发明也被当做发现时，倾向于它是一种发现吧。尝试把自己想象成让这些事物自然而然成为自己连向世界的通道。
(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，挑选要做的事是个例外。这个过程是一个发现，但是最好的情况下它将是一种发明。最好的情况是你在发现它的过程中发明了一个领域。）
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.
类似的，如果你在尝试建造一个强大的工具，那就不要为它设定上限。一个强大的工具在理论上是会以你没有预见的方式被使用的，所以去除限制吧，就算你还不清楚这样做的好处是什么。
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.
伟业总是像工具一样提供一个给他人继续向上搭建的平台。所以若你是在发明新的点子为人所用，或是提出他人可以回答的问题，这都是好事。最好的想法在各种领域都有好的启示。
If you express your ideas in the most general form, they’ll be truer than you intended.
如果你把你的想法用最基本的方法表达，它们将比你想要表达的更加真实诚恳。
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，单单真实是不够的。伟大的想法得真实，也得新颖。而且，即使你已经学到了足够多的知识，甚至达到了某些知识领域的顶峰，你也还需要拥有某种能力，才能发现新的想法。
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，我们会把这样的能力区分开来，分别叫它们：原创性、创造力和想象力。乍一想，这样的区分很合理，因为它们在某种程度上确实是独立的技能。你完全可能拥有很强的专业能力，但并不具备创造能力。
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.
我从来不喜欢「创造的过程」这个词。它有一定的误导性。创造不是一个过程，而是一种思维习惯。具有独创思维的人，对于他们关注的任何事物，都能不断产生新的想法，就像一个角磨机会发出火花一样，他们生来如此。
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.
不过，如果他们不太了解自己所关注的事情，产生的新想法可能不会太好。我认识的具有独创思维的人之一在离婚后，决定专注于约会，但他对约会的了解大致与一个 15 岁的普通人相当，这带来了非常多「离谱」的经历。但他的经历也更清晰地展现了独创力在没有专业性支持的时候，会是什么样子。
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. [15]
尽管我不知道人能不能培养自己的原创性，但一个人肯定有办法充分利用自己已有的能力。例如，当你手上有别的事要处理的时候，反倒容易有新的点子。新想法不是靠冥思苦想出来的，而是你在构建或理解一些难度稍高的事物的过程中，自然而然收获的产物。[15]
[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.
[15] 显然，灵感到来的时候你不一定正在工作，但你很可能最近一直在忙于工作。
Talking 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.
谈论或书写你感兴趣的事情是产生新想法的好方法。当你试图描述那个想法时，你就会不断从心底里找出词语，填补出它的模样。事实上，有一些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. [16]
改变你身处的环境可能会有所帮助。新想法常常在你去到新的地方时蹦出来，因为旅程本身就能激发这些想法。而且你可能不需要走太远，有时候，只是出去散散步就够了。[16]
[16] Some say psychoactive drugs have a similar effect. I’m skeptical, but also almost totally ignorant of their effects.
[16] 有人说精神活性药物有类似的效果。我持怀疑态度，不过得承认，我对它们的效果几乎一无所知。
It 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.
在关联主题下漫游，也会很有帮助。这是因为当你在探索那些相关话题的时候，就给自己的创意机器提供了更多素材，新想法常常隐匿在事物的内在联系之中。
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. [17]
不要把你的注意力平均分配在每个话题上，因为那会导致任何一个话题都得不到足够的关注。你应该根据某种类似于幂律（Power Law）的法则[17]来分配精力。
[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.
[17] 例如，你可以将第 n 个最重要的主题的注意力分配为 (m-1)/m^n，其中 m > 1 。当然，你无法如此精确地分配你的注意力，但这个公式起码给你提供了一些合理分配的灵感。
Be professionally curious about a few topics and idly curious about many more.
对于一些话题要保持专业上的好奇心，对于更多的话题则保持随意的好奇心就够了。
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.
好奇心和原创性密切相关。好奇心为独创性提供了源源不断的新事物。更进一步来讲，好奇心本身就是原创性的表现形式之一。问题之于答案，正如好奇心之于原创性，因为好的问题本身就是答案的一部分，强大的好奇心本身也是创造。
定义好点子
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?
寻找新想法是一种奇怪的游戏，因为它就像是对着你眼前的事物挑刺儿。一旦你想出一个新想法，你往往会讶异于它有多平常而熟悉，以至于你会想，为什么以前没有人想到这一点呢？
When an idea seems simultaneously novel and obvious, it’s probably a good one.
当一个想法既陌生又熟悉的时候，它很可能就是一个好点子。
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.
留意到显而易见的事物听起来很简单。然而，从经验上讲，产生新想法却很困难。这一对矛盾的根源是什么呢？捕获新想法通常需要你改变看待世界的方式。我们通过不同的心智模型来看待世界，这些心智模型既帮助了我们，又限制了我们。当错误的心智模型改变了，新的想法就变得显而易见。但是，看见并修复错误的心智模型并不容易。这就是为什么新的想法既显而易见又难以发现的原因：你得先拨开云雾，才能见月明。
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.
发现心智模型错误的方法之一，是比别人都更严谨。错误的看待世界模型会在与现实碰撞的过程中留下线索，但大多数人并不愿意直视它。由于他们的思考全仰仗于已有的心智模型，他们往往会选择忽视那些线索，无论那些线索在回顾时看起来多么明显。
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.
要找到新的想法，你必须捕捉到那些线索的蛛丝马迹，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（Maxwell’s equation）的广阔前景，不仅仅是因为他在持续寻找新想法，还因为他更加严谨。
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.
此外，你还得愿意打破规则。尽管打破规则和观察严谨听起来有些矛盾。如果你习惯于打破规则，你就更容易修正自己看待世界的心智模型。因为在所有通过旧模型认识世界的人看来，新模型都打破了原先的规则。
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.
很少有人理解打破规则有多难，因为当人们接受了新想法的一瞬间，它就落入窠臼了。一旦你开始通过新的心智模型来认识世界，一切看起来都会非常合理。但在这之前，你认识的世界并非如此。比方说，过去了大半个世纪，日心说才被广泛接受。即便在天文学家当中也是如此，因为「日心说」太有悖于直觉了。
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.
实际上，如果你仔细思考一下，一个好的新想法必须在大多数人看来都是糟糕的，不然别人早就去尝试了。所以，你要寻找的是那些乍看很疯但实则正确的想法。如何辨别这些想法呢？对此，我们无法给出定论。通常，看起来糟糕的想法确实很糟糕。但是，那些实则正确的疯狂想法，往往令人兴奋、影响深远；而那些纯粹糟糕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.
有两种方式可以轻松打破常规的方法：享受打破规则和完全对规则漠不关心。我分别称这两种情况为，积极地独立思考和消极地独立思考。
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.
那些极具独立思考能力的人往往不会循规蹈矩。规则不仅无法阻止他们，反而会激发他们更多的能量。对于这类人来说，有时候，光是项目本身的难度所激起的愉悦，就足以让他们开始行动了。
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.
打破常规的另一种方式是不在乎它们，甚至不考虑它们的存在。这就是为什么新手和外行经常会有新的发现。不知道某个领域那些预设的前提，使得他们能够被动地独立思考。貌似阿斯伯格症患者也不容易被传统观念影响，我认识的好几位都说这一点能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.
严谨加上打破常规听起来像是一个奇怪的组合。在流行文化中，它们是对立的。但在这方面，流行文化自带一个错误假设。它假设所有议题都是稀松平常的，而在稀松平常的事情上，严谨和打破常规是对立的。但是，在真正重要的议题上，只有真正严谨的人才能打破常规。
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.
一个容易被忽视的想法通常挺到半决赛才会被彻底忽视。你在潜意识中确实看到了它，但是你的另一部分潜意识却否定了它，因为它太奇怪、太冒险、太费力、太有争议性了。这暗示了一个令人兴奋的可能性：如果你能摘下这些有色眼镜，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.
有一种方法可以避免你的潜意识为了保护你而否定你，那就是去追问：有什么好想法值得别人去探索？
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.
你还可以通过从相反的方向开始，发现那些容易被忽视的想法：从发现遮蔽它们的东西开始。每个备受珍视但错误的原则，都被一片有价值却未被认真检视过的想法所包围，因为它们有悖于那些实际错误的原则。
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. [18]
宗教就是由一系列备受珍视但错误的的原则组成的。因此，任何字面或者实际意义上的「宗教」，其背后都有很多有价值但从未被认真检视过的想法。哥白尼和达尔文的发现均属此类。[18]
[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.
[18] 任何宗教的宗则都一定是会引起分歧的。否则任何人都可以接受这些信仰，那么这些宗教的信徒就无法与把自己与其他人区分开来了。
What 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?
在你所从事的领域，人们对什么事情有宗教般的执着，即对某些原则过于依赖，而这些原则可能并不像他们想象的那样不言自明？如果你放弃这些原则，会产生哪些可能性呢？
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.
人们在解决问题上比决定要解决哪些问题更具创意。即使是最聪明的人，在决定要解决什么问题时也会出人意料地保守。那些在其他方面从不随大流的人，也会上赶着去解决最受关注的那些问题。
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更保守的一个原因是：问题是更大的赌注。一个问题耗费你的时间常常以年计算，而找到解决方案花费的时间往往以天计算。但即便如此，我认为大多数人还是太保守了。他们为了规避风险，迎合潮流，那些冷门难题的价值被低估了。
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.
冷门难题里最有趣的一种，就是那些大家都以为已经被充分讨论过、但实际上并没有被讨论到底的问题。做出伟大的事业的人，往往会挖掘并展示出已有事物的潜力。艺术家丢勒和发明家瓦特都做到了这一点。所以，如果你对一个别人都以为被挖得不能再挖的领域感兴趣，不要因此动摇信念。在这一点上，他们往往是错的。
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.
解决冷门问题也可以非常令人愉悦。没有漫天的吆喝声，也不用着急。机会主义者和评论家都在忙于其他事情。那些已有的事物也不会有什么变数。此外，其实想到了就是赚到了，因为不去琢磨的话，这些想法就会被白白浪费掉。
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.
但一个问题之所以会被忽视，并不是因为它平凡。它只是看起来没有它实际上那么重要。那怎么找到这些问题呢？放飞自我 —— 让好奇心带领你去探索，至少暂时忽略那个说着「你只应该解决『重要』问题」的声音。
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.
你确实需要解决重要的问题，但几乎每个人在判断问题重要程度上都过于保守。如果你周围有一个重要但被忽视的问题，那么在你的潜意识里，你已经注意到了。所以，试着问问自己：如果你停下「正经」的工作，纯粹出于好玩，你会去做什么？这个答案可能比它看上去重要得多。
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.
比起选择解决方法，选择解决什么样问题更需要原创思维。那些发现全新领域的人，正是因此而不凡。因此，选择要解决的问题看似只是在起步阶段的决定要干什么，实际上却是整个游戏的关键所在。
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.
很少人能理解到这一层。对于如何找到「新想法」大家最大的误解之一，就是忽视了「问题」对于「答案」的重要性。人们总觉得想出伟大的想法就是找到了答案，但真正的关键在于提出怎样的问题。
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.
我们之所以会低估「问题」的重要性，是因为受到了学校的影响。在学校里，问题的存在不过是为了被回答的那一瞬间，就像不稳定的粒子一样。但是，一个真正的好问题的作用远大于此。一个真正的好问题本身就是新发现的一个部分。比如说，新物种是如何产生的？物体落地受的力和行星保持轨道受的力是一回事吗？光是提出这样的问题，你就已经踏入令人兴奋的新领域了。
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.
悬而未决的问题可能会让人感到不舒服，但这样的问题你想得越多，就越有可能找到解法 —— 或者说，更令人兴奋的是，你会发现那些悬而未决的问题竟然有共通之处。
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. [19]
有时候，你会花很长的时间思考一个问题。伟大的工作往往始于你多年前就开始关注、但一直没有停止思考的问题，有的甚至始于小时候的观察。人们经常谈论保持年轻时梦想的重要性，但同样重要的是持续思考年轻时关注的问题。[19]
[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.
[19] 或许写下一份你年轻时曾经好奇的问题清单是个不错的练习，你可能会发现现在你有能力去解答其中的一些问题了。
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.
这一点在专业领域中也有体现。人们总觉得专家什么都懂，其实并不是这样。对专家来说，好的问题往往有两个特征：a）这个令人困惑的问题足够重要；b）其他人也搞不明白。
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. [20]
想象一下，在新想法被发现之前的那一刻发生了什么吧。有足够专业知识的人，总会对某件事感到困惑。这意味着困惑是原创性的组成部分。只有当你接受世界就是充满谜团的这个事实，你才愿意去直视它们。不过你不能就这样照单全收，以至于自己无法产生解决它们的动力。[20]
[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.
The best lack all conviction, while the worst，Are full of passionate intensity.
[20] 原创性和不确定性之间的联系导致了一个奇怪的现象：因为传统思维者比独立思考者对自己更加确信，所以他们在争论中往往占据上风，尽管他们通常更愚蠢。
最好的人缺乏信念，而最坏的人充满激情。
It’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.
拥有成堆的未解之谜是一件很棒的事。而这正是那种富人越富的情况，使得获取新问题的最佳方式就是尝试回答现有的问题。问题不仅能指引我们找到答案，还会带来更多值得思考的问题。
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.
最好的问题在不断的回答中生长。也许你注意到当前的死板公式中突出来一条线索，并试着拉扯，结果它就变得越来越长。所以在尝试回答之前，无需要求问题有多宏大，你也很难预测到这一点。要注意到线索已经够难了，更不用说去预测拉扯的话将会有多少东西迎刃而解。
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.
最好是有些狂野的好奇心，轻轻地拉扯很多线索，看看会发生什么。大事始于细微之处。它的最初版本通常只是实验、副课题或一小场谈话，一切从这里逐渐发展成为更大的事情。所以，多让小事发生。
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. [21]
高产的重要性往往被低估了。你尝试的不同事情越多，发现新事物的机会就越大。不过要明白，尝试很多事情也意味着会有很多行不通的部分。你无法在不遇到坏点子的情况下直接想到好点子。[21]
[21] Derived from Linus Pauling’s “If you want to have good ideas, you must have many ideas.”
[21] 来自化学家林纳斯・鲍林： 「如果你想要有好的创意，你就要先有很多创意。」
Though 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.
虽然先研究前人的工作，听起来像是更负责任的做法，但通过把手弄脏，你会学得更快且更加乐趣盎然，而且你会对前人的作品有更好的理解。所以，尽快开始是好的，且从小规模开始，从简单的小事开始，才能聚沙成塔。
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.
如何从小事开始，做成伟大之事？答案是不断迭代。伟大的作品几乎总是通过不断推出新版本来完成的。从小事开始，逐渐演化，最终版会比你原先计划的更加智慧、更有野心。
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.
如果你的产品做出来是给别人用的，持续迭代就尤为有用 —— 要快速呈现初始版本，并根据用户的反馈不断改进。
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.
从最小可用的产品开始。而令人惊讶的是，这些小产品确实可用。就算不行，这也至少让你迈出了第一步。
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内容。对于第一个版本来说，这样做有一个名字（拖了太久发布），对于第二个版本来说，这样做也有一个名字（第二系统效应）——不过这两者都只是试图添加太多新内容的具体例子而已。
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. [22]
一个新项目的早期版本，有时会因基础得如同玩具而被忽视。但其实当人们这样做时，是一个好兆头。这意味着它具备了一个新想法所需的一切，只是缺乏规模，而规模往往会随之而来。[22]
[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.
[22] 将一个项目称为 「玩具」 就像在说一份表述「不恰当」一样。这意味着不会再有更多实质性的批评了。
The 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.
与从小事开始并逐步迭代相反，另一种选择是事先计划好你要做的事情。通常来说，计划似乎是更负责任的选择。说「我们要先做 x，然后做 y，最后做 z」听起来比说「我们试试 x，看看会发生什么」更有条理，但是它效果却没有后者那么好。
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.
计划本身并不是好事。有时候计划的确有必要，但它不过是一种「必要的恶」，是对无法避开的条件的回应。你必须做计划，是因为你在使用不灵活的工具，或者因为你需要协调很多人的努力。如果你保持小规模项目，并使用可变通的工具，你就不需要做太多的计划，你的设计可以逐步发展。
与年龄无关
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.
尽可能多地在你的承受范围内承担风险。在一个有效的市场中，风险与回报是成正比的，所以，不要寻求确定性，而是要寻找那些预期收益更高的赌注。如果你没有时不时就经历失败，那你可能是过于保守了。
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.
尽管年长的人通常更为保守，但其实年轻人更常犯这个错误。缺乏经验使他们害怕冒险，但实际上正是因为年轻，你才能承担最多的风险。
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有价值。在推进项目的过程中，你会经历很少有人见过的领域，并遇到很少有人提出的问题。而且，就找到值得思考的问题而言，「尝试难度稍高的事情」可以说是最好的方式。
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，要充分利用年轻的优势；当你年长时，要善用年长的优势。年轻的优势包括活力、时间、乐观和自由；年长的优势则是知识、高效、财富和权力。而通过努力奋斗，年轻时可以获得一些后者的优势，并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.
年长之人胜在「知道自己有哪些优势」。年轻人常常拥有优势而不自知。年轻人最大的优势可能就是时间了，但他们并不知道自己所拥有的时间多得超乎想象。而把时间转化为优势的最佳方式，是以稍微随意的方式利用它：仅仅出于好奇，多去了解一些好像你不需要了解的事情，尝试搞一些很酷的事物，或者成为某个领域的超级高手。
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. [23]
「稍微」是一个重要的限定词。年轻时可以挥霍时间，但不要简单地浪费它。在做一些你担心可能是浪费时间的事情，和在做一些你确信会浪费时间的事情，这两者区别很大。前者至少是一个赌注，而且可能带来比你的想象中更好的结果。[23]
[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.
[23] 判断你是否在浪费时间的其中一种方法是问自己：「你是在创造还是在消费」。编写电脑游戏比玩游戏更不容易浪费时间，而玩那些你可以创造东西的游戏比玩那些不能创造的游戏更不容易浪费时间。
The 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. [24]
年轻最微妙的优势，或者更准确地说是因「缺乏经验」而有的优势，就是能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，有时并不能完全接受它。这问题通常出在你的大脑，不过偶尔也可能是想法本身的问题。这个时候，那个想法就会像一根刺似的，每每在你思考时就会让你无所适从。熟悉这个想法的人早已接受了这种不适，但你可以选择不接受。[24]
[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.
[24] 另一个相关的优势是，如果你还没有公开发表任何言论，你就不会对支持你先前结论的证据产生偏好。在这方面，只要你足够诚实客观，你就可以保持永远年轻的心态。不过这很少有人能做到。对于大多数人来说，先前发表的观点会对自己产生类似意识形态的影响，只是在数量和程度上有所差异。
So 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，当你第一次学习某个东西时，要注意那些看起来不对或缺失的地方。你可能会有忽略它们的冲动，因为 99% 的情况下问题出在你自己身上。而且，为了继续往下学，你可能不得不暂时搁置自己的困惑。但别忘了它们。当你对这个主题有了更深入的了解后，回过头来看看自己是否还有困惑。如果在你现有的认知下，那些你还是感到困惑，那么，这很可能是代表你拥有了一个全新的想法。
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知识之一，就是知道你不必担心什么。年轻人知道什么事情很要紧，但不知道它们分别有多重要。因此，他们平等地为每一件事焦虑。而实际上，值得他们操心的事情只有一部分，剩下的几乎不值一提。
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.
年少无知的问题不仅在于「你不知道什么」，还在于「你所知的并非如你所想象」。成年的你会发现，你的脑子积攒了一大堆无意义的东西，比如，糟糕的习惯、错误的观念。不清理掉这些，你不可能做出伟大的事业。
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.
你脑子里的许多错误观念都是学校留下的。我们对学校太习以为常，以至于不自觉地把上学和学习等同起来，但事实上，学校有各种奇怪的特点，扭曲了我们对学习和思考的认知。
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，学校引导我们进行被动学习。自从你还是个小孩，就有一个权威人物站在教室前面，告诉所有人必须学习什么，并统一衡量你是否学会了。但是，课程和考试并不是学习的本质，它们只是学校设计出来的通用产物。
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.
越早克服这种被动性越好。如果你还在上学，试着把上学看作是自己主导的项目，把老师看作在为你工作，而不是反过来。听起来可能有点牵强，但这不仅仅是一个思维实验。从商业的角度看，这就是事实。以及，在最理想的情况下，这也是教育的本质。最好的老师不会想成为你的老板。他们更希望你主动向前探索，把老师当作可以求助的对象，而不是一味地被老师带着走。
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.
学校也会错误地塑造你对工作的认识。在学校里，他们总是告诉你要解决什么问题，并且你几乎总是可以用目前所学的知识解决。而在现实生活中，你必须弄清楚问题是什么，而且常常不知道自己能否解决。
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.
但学校最糟糕的影响，就是让你把「搞定考试」约等于「赢得一切」。用这种思维，你不可能做得出一番伟大的事业。你瞒不了天，也瞒不了地。所以，停止寻找捷径。战胜体制的方法是专注于别人忽视的问题，并找到解决方案，而不是省去工作本身。
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.
不要认为自己需要依赖别人给你「机会」。即使他们能给你机会，但获得机会的最佳方式依然是专注于做出好成绩，而不是跟在有影响力的人后面。
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.
不要对权威的拒绝太过在意。给招生官员和奖项评审委员会留下深刻印象的品质，与做出色工作所需的品质是完全不同的。那些权威评选委员会的决定，只有在它们作为反馈循环的一部分时才具有意义，而这种情况并不多。
模仿不屈从
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.
刚接触某个领域的人，通常会先模仿现有的作品。这没什么不好的，没有比「通过尝试模仿来学习某样东西如何运作」更好的方法了。而且，复制并不一定意味着你的作品缺乏原创性。原创性关键在于新想法的存在，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. [25]
不过，模仿也分为好模仿和坏模仿。如果你要模仿某件作品，那就公开做而不是偷偷摸摸地，更不要无意识地复制。这就是那句常被误用的名言「伟大的艺术家都会抄袭」所指出的问题。真正危险的模仿是一板一眼毫无灵魂的复制，会导致你染上抄袭污名，因为你不过只是一辆沿着别人铺设轨道行驶的火车。不过，还有一种极端情况，即使你模仿前人，也可以青出于蓝而胜于蓝。[25]
[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.
[25] 在 17 世纪 30 年代初，丹尼尔・迈滕斯绘制了一幅画，描绘了亨利埃塔・玛丽亚将月桂花环递给查理一世的一幕。画家范・戴克随后绘制了自己的版本，以展示他的绘画技巧更加出色。
In 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，几乎不可避免地，你的早期工作要在他人的工作成果之上进行开展。项目也好，研究也好，很少是横空出世的，它们往往是对先前工作的补充或者进一步研究。当你刚开始起步时，你没有任何自己的作品作为参照物，只能先基于其他人的研究或者成果开展工作。一旦你在这个领域有所建树，你就可以基于自己的成果进一步开拓。尽管人们往往推崇后一种工作方式，诟病前者缺乏原创性，但事实上，这两者没什么太大区别。
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.
很有趣的是，那些最新奇的想法，常常会因为它们的新奇之处被视为缺乏原创性的衍生品。甚至连发现者本人，也常常会把自己的新发现看成是现有事物的变体，因为这些发现太新了，还没有更合适的概念来描述它们。
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.
模仿确实存在一些危险。比如说，你往往会抄袭一些陈旧的东西——它们在当年曾经是先锋代表，但现在早就过时了。
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.
当你试图模仿的时候，不要刻板地全盘照抄，有些东西一比一照抄会让你看起来滑稽可笑，比如如果你只有 18 岁，但你却模仿一位 50 岁杰出教授的举止，或者使用文艺复兴时期的俗语谈话。
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.
那些你欣赏的人身上肯定存在着一些缺点，尽管如此，他们还是成功了。但他们身上最容易模仿的部分，往往就是这些缺点。
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.
这在言行举止方面尤为真实。比如说，一些有才华的人是混蛋，这有时会让缺乏经验的人误以为，想成为一个有才华的人，我得先成为一个混蛋。但事实并非如此，才华只是让人们愿意勉强忍受他们混蛋一面的理由。
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.
最强大的模仿借鉴方式之一，就是将某样事物从一个领域复制到另一个领域。历史上充满了这种偶然发现的故事，所以，通过有意识地学习其他类型的工作，或许能够帮助我们增加发现新事物的机会。如果你相信这点，那么你可以广泛地从其他不同领域中汲取灵感。
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.
负面的例子可以像正面的例子一样具有启发性。有时候相比做得好的事情，你可以搞砸的事情中学到更多。有时候，只有在缺少什么的时候才能清楚地知道需要什么。
寻找同行人
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. [26]
如果你所在领域的大量顶尖人才聚集在同一个地方，那么去那里待上一段时间通常是个好主意。这不仅会让你变得更有雄心壮志，也会让你逐渐对这些所谓的人才祛魅，了解到他们也只是普通人。这个过程会让你变得更有自信。[26]
[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.
[26] 我其实一直故意对「地方」的定义含糊不清。截至目前，身处同一物理空间确实有难以复制的优势，但这种情况可能会改变。
If 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.
如果你足够真诚，你大概会比自己预想的得到更加热烈的欢迎。大多数擅长某个领域的人都乐意与对这个领域真正感兴趣的人交谈。如果这些擅长者在工作上也非常出色，那么他们大概率会把工作当成自己的爱好，而人总是喜欢谈论自己的爱好的。
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.
不过你可能需要花费一些功夫才能找到真正优秀的人。在有些地方，尤其是大学，做出伟业会非常有威望。所以人人往往以为，这里的每个人都在努力做出伟大的事业。但事实上并非如此。大学内部人士无法公开告诉你，不同院系或者部门的水平差异巨大。有的院系拥有正在从事伟大工作的杰出人才；有些院系过去有过这样的人才；而有些院系从来都只是平庸。
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.
寻找最好的同伴。有很多项目是无法独自完成的，即使你在做一个想要独立完成的项目，能有其他人鼓励你并为你提供建议也是一件好事。
Colleagues don’t just affect your work, though; they also affect you. So work with people you want to become like, because you will.
同伴不仅仅影响你的工作，他们也会影响你自己的为人。所以，去和那些你想成为的人一起做事吧，因为你会变得像他们一样。
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.
这些同伴的质量远比数量更重要。拥有一两个优秀的同伴要好过拥有一大群还不错的同伴。事实上，前者不仅只是比后者更好，而且还是想做出伟大事业的必须条件。从历史来看：伟大的工作往往诞生于杰出的群体当中。这说明了，你与谁共事往往决定了你是否能够做出伟大的事。
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.
如何知道你有足够好的同伴？根据我的经验，当你真的拥有的时候，你自然会知道的。这意味着，如果你无法确定自己有没有好同伴，那你大概是没有的。也许我可以给出一个更具体的答案，比如说，足够好的同伴会提供令人惊讶的洞察。他们能够看到和做到你所不能的事情。所以，如果你有一些足够好的能够在这个意义上让你保持警惕，那你所在的职场环境是符合标准的。
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. [27]
我们大多数人都可以从与同伴的合作中受益，但有些项目需要更多人，而且启动这样的项目并非人人都适合。如果你想要运营这样的项目，你就必须成为一名管理者。而优秀的管理能力和其他任何工作一样需要一定的才能和兴趣。如果你没有这些，就没有中间道路可选：你要么强迫自己学习管理作为「第二语言」，要么避免这样需要自己成为管理者的项目。[27]
[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.
[27] 当其他人需要做的工作非常受限时，比如 SETI@home 或比特币，这种说法就是错误的。而通过给予原行动准则的各个节点更大自由度，这种说法的适用范围可能会有所扩大。
保持高士气
Husband 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.
珍视你的士气。如果你在做的事既耗时又费力，那士气就是成事的基础。你必须用心培养、小心呵护。
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.
好的士气始于好的生活观。如果你是一个乐观主义者，你更有可能做出出色的事业；如果你认为自己是幸运儿，而不是倒霉蛋，你也更有可能做成出色的事业。
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.
确实，做自己的事在一定程度上可以保护你免受难题的困扰。如果你选择做比较纯粹的事，它的难度本身就会成为你逃离日常生活难题的避风港。如果你要说这是在逃避现实，那确实也算，不过它的确非常有效，一些历史上最伟大的思想家都是这么做的。
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.
一个人的士气可以通过做事本身来得到提升：士气高能帮你做成事儿，做成事儿又能进一步提升你的自信，让你做得更好。不过要注意，这个循环也可以反向运作：如果你做得不好，这可能会使你状态低落，使你更难以做好这件事。由于这个循环决定了你是否在朝着正确的方向运行，当你陷入困境时，可以试着先着手于更容易的小事，这样你就能完成一些事情了。
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.
雄心勃勃的人们常犯的一个错误就是让挫折彻底摧毁他们的状态，就像气球被扎破了一样。想避免这种状态，你可以明确地把挫折视为做大事过程中必不可少的一部分，毕竟，解决难题总是一个螺旋上升的过程。
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.
做出伟大事业的过程和深度优先搜索（DFS）算法类似，你的渴望相当于一个根节点（Root Node）。你应该以你的渴望为原点，尽可能地探索每一种可能性。所以，「如果一开始没有成功，就再试一次」这种说法并不完全正确。它应该是：如果一开始没有成功，要么再试一次，要么退回一步再试一次。
“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，有时候选择退出是正确的。所以，更准确的表述应该是：永远不要让挫折，令你做出超过必要限度的退让。进一步而言：永远不要放弃根节点，不要放弃你的渴望。
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.
如果你做的事令你感到痛苦，这并不一定是个坏兆头，就像跑步时喘不过气也不一定是坏兆头一样，因为这取决于你跑得有多快。所以，要学会区分好的疼痛和坏的疼痛。好的疼痛是努力的象征，坏的疼痛是损伤的象征。
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.
受众是你士气的重要组成部分。如果你是学者，你的受众可能是你的同行；如果你在艺术领域，你的受众可能就是传统意义上的观众。无论如何，你不需要追求受众的数量。受众的价值与其规模并不成正比。这对于名人来说是个坏消息，但对于刚刚起步的人来说是个好消息，因为这意味着有一个小而忠诚的受众群体就足以支持你了。如果能有一小撮人真心喜欢你所做的事情，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. [28]
你和你的受众之间，应该尽可能地没有第三方。在某些工作中，这是不可避免的，但是摆脱这种情况会让你感到非常自由。如果可能的话，最好切换到不需要第三方的工作中，这样你就可以直接与受众交流。[28]
[28] Corollary: Building something that enables people to go around intermediaries and engage directly with their audience is probably a good idea.
[28] 推论：建立一个让人们能够绕过中间人直接与他们的受众互动的事物，可能会是一个好主意。
The 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.
与你相处的人也会很影响你的士气。有些人能给你补充能量，而有些人会消耗你的能量，而且你并不知道一个人会对你产生的影响会是什么样。去寻找那些为你补充能量的人，避免和那些消耗你能量的人打交道。当然，如果有你需要照顾的人，那就优先考虑照顾他们。
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.
如果一个人不理解工作对你的重要性，不要和他结婚；如果一个人把工作看成和他抢夺你注意力的竞争对手，不要选择这样的伴侣。如果你有抱负，你就需要工作，这几乎是必然的；所以，一个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. [29]
最终，一个人的士气是与身体相关的。你需要用身体思考，所以保证身体健康至关重要。这意味着你应该坚持定期锻炼、良好的饮食和睡眠，避免使用危险的药物。跑步和散步是特别好的锻炼方式，因为它们有助于思考。[29]
[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.
[29] 始终沿同一条路线走可能会有所帮助，因为这样可以释放大脑的算力。对我来说是这样的，而且也有一些历史证据支持这一观点。
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.
做成一件大事的人不一定比其他人更快乐，但他们肯定比没做成这件事的自己更快乐。事实上，如果你是一个聪明又有野心的人，在工作中得过且过，反而可能是件危险的事情。因为如果聪明又有野心的人没能取得太多成就，他们往往会变得愤世嫉俗。
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.
想要给别人留下好印象没有问题，但要选择正确的人。你尊敬的人的意见才是重要的意见。名声，说白了只是某个对你来说无足轻重的群体的意见，它只会带来噪音。
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.
事业的声望最多只能作为一个滞后的指标，它有时甚至是完全错误的。如果你做得足够好，你所做的事就会自然变得受人尊重。所以，对于一份事业，你应该问的问题不是从事它能收获多少声望，而是你能将它做得有多好。
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.
竞争可以是一种有效的激励因素，但不要让它为你选择你要解决的问题；不要因为别人在追逐某事而让自己被卷入其中。事实上，除了更加努力地工作，不要让竞争对手对你产生任何实质性的影响。
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。你的好奇心从不撒谎，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.”
注意到「好奇心」这个词出现的频率有多高。如果你问一位先知如何做出伟大的工作，而先知只回答一个词，那我会押注是 「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.
当然，保持好奇这并不能直接转化为行动建议。因为仅仅有好奇心是不够的，而且你也无法控制好奇心。但你可以培养它，并让它带领你前进。
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.
好奇心是做出一番伟大事业的关键，它将为你选择你从事的领域，带你走向领域前沿，让你注意到领域中的空白，并驱使你去探索。完成伟大的事业的过程，就像是与好奇心共舞。
渴望做大事
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，但我已经尽可能浓缩这篇文章的篇幅了。不过最起码，它的长度起到了一个筛选的作用。如果你能读到这里，那么你一定对做出伟大的事业非常感兴趣。若是的确如此，那么你已经比你自己意识到的更进一步了。
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?
毕竟这个世界上真正愿意追求卓越的人，是很少很少的。 完成伟大事业的影响因素指的是字面上的、统计意义上的因素，它们包括：能力、兴趣、努力和运气。运气是无法控制的，我们忽略它。我们同时也假设，如果你确实想要做出伟业，努力是必然的。所以问题终将归结到你的能力和兴趣上。你能否找到一种工作，能将你的能力和兴趣结合起来，产生一系列新的想法？
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.
我们有理由保持乐观。因为我们有很多不同的方式可以做出伟大的事业，甚至还有更多尚未被发现的方法。在所有这些不同类型的事情中，最适合你的那件事，可能是一个你认为相当匹配的选择，也可能是一个你都意想不到但也十分合适的选择。剩下的问题是如何找到它，以及你的能力和兴趣能够带你走多远，不过这些问题只能通过付出行动来回答了。
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.
有很多人尝试过做出伟大的事，但实际上做出伟大事业的人并不多。阻碍他们的，是谦逊和恐惧。想要成为下一个牛顿或莎士比亚似乎是件痴人说梦的事情，看起来几乎不可能实现。如果去做这样的尝试，似乎注定会一败涂地。但是尽管如此，也没有人会下定决心放弃完成伟大的事。他们只是在潜意识里打退堂鼓：他们在逃避做成伟业的难度本身。 所以，现在我要问你一个问题：这辈子你想不想做出伟大的事？现在立刻马上，给出你的答案。
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.
我一般不会这样要求我的读者，但我知道，你内心对这件事情是有渴望的（不然你也不会读到这里了）。
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.
不要担心自己是否显得过于自以为是。你不必将这个答案告诉任何人。如果事情太难，你失败了又怎样？很多人的问题比这个问题糟糕多了。事实上，如果「失败了怎么办」是你最糟糕的问题，那你算幸运的了。
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，你不得不努力工作。但是，很多人都不得不努力工作。如果你觉得你正在从事的工作非常有意思（当然，如果你走在正确的道路上你一定会觉得它有意思的），那么，你在工作中可能会比你绝大多数同行更加得心应手。
The discoveries are out there, waiting to be made. Why not by you?
伟大的事业就在那里等待被实现，为什么那个实现的人不能是你呢？
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 Neilsen, Courtenay Pipkin, Joris Poort, Mieke Roos, Rajat Suri, Harj Taggar, Garry Tan, and my younger son for suggestions and for reading drafts.
致谢：Trevor Blackwell、Daniel Gackle、Pam Graham、Tom Howard、Patrick Hsu、Steve Huffman、Jessica Livingston、Henry Lloyd-Baker、Bob Metcalfe、Ben Miller、Robert Morris、Michael Neilsen、Courtenay Pipkin、Joris Poort、Mieke Roos、Rajat Suri、Harj Taggar、Garry Tan 以及我的小儿子对本文的支持与建议。