{"source":"smry-fast","cacheURL":"https://paulgraham.com/greatwork.html","article":{"title":"How to Do Great Work","resolvedUrl":"https://paulgraham.com/greatwork.html","byline":null,"dir":"ltr","lang":"","content":"


\"How

July 2023

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

Partly my goal was to create a guide that could be used by someone\nworking in any field. But I was also curious about the shape of the\nintersection. And one thing this exercise shows is that it does\nhave a definite shape; it's not just a point labelled \"work hard.\"

The following recipe assumes you're very ambitious.

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

In practice you don't have to worry much about the third criterion.\nAmbitious people are if anything already too conservative about it.\nSo all you need to do is find something you have an aptitude for\nand great interest in.\n[1]

That sounds straightforward, but it's often quite difficult. When\nyou're young you don't know what you're good at or what different\nkinds of work are like. Some kinds of work you end up doing may not\neven exist yet. So while some people know what they want to do at\n14, most have to figure it out.

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

Develop a habit of working on your own projects. Don't let \"work\"\nmean something other people tell you to do. If you do manage to do\ngreat work one day, it will probably be on a project of your own.\nIt may be within some bigger project, but you'll be driving your\npart of it.

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

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

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

Once you've found something you're excessively interested in, the\nnext step is to learn enough about it to get you to one of the\nfrontiers of knowledge. Knowledge expands fractally, and from a\ndistance its edges look smooth, but once you learn enough to get\nclose to one, they turn out to be full of gaps.

The next step is to notice them. This takes some skill, because\nyour brain wants to ignore such gaps in order to make a simpler\nmodel of the world. Many discoveries have come from asking questions\nabout things that everyone else took for granted. \n[2]

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

Boldly chase outlier ideas, even if other people aren't interested\nin them — in fact, especially if they aren't. If you're excited\nabout some possibility that everyone else ignores, and you have\nenough expertise to say precisely what they're all overlooking,\nthat's as good a bet as you'll find.\n[3]

Four steps: choose a field, learn enough to get to the frontier,\nnotice gaps, explore promising ones. This is how practically everyone\nwho's done great work has done it, from painters to physicists.

Steps two and four will require hard work. It may not be possible\nto prove that you have to work hard to do great things, but the\nempirical evidence is on the scale of the evidence for mortality.\nThat's why it's essential to work on something you're deeply\ninterested in. Interest will drive you to work harder than mere\ndiligence ever could.

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

The big prize is to discover a new fractal bud. You notice a crack\nin the surface of knowledge, pry it open, and there's a whole world\ninside.

Let's talk a little more about the complicated business of figuring\nout what to work on. The main reason it's hard is that you can't\ntell what most kinds of work are like except by doing them. Which\nmeans the four steps overlap: you may have to work at something for\nyears before you know how much you like it or how good you are at\nit. And in the meantime you're not doing, and thus not learning\nabout, most other kinds of work. So in the worst case you choose\nlate based on very incomplete information.\n[4]

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

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

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

What should you do if you're young and ambitious but don't know\nwhat to work on? What you should not do is drift along passively,\nassuming the problem will solve itself. You need to take action.\nBut there is no systematic procedure you can follow. When you read\nbiographies of people who've done great work, it's remarkable how\nmuch luck is involved. They discover what to work on as a result\nof a chance meeting, or by reading a book they happen to pick up.\nSo you need to make yourself a big target for luck, and the way to\ndo that is to be curious. Try lots of things, meet lots of people,\nread lots of books, ask lots of questions.\n[5]

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

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

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

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

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

This should follow from the excitingness rule. Obviously the most\nexciting story to write will be the one you want to read. The reason\nI mention this case explicitly is that so many people get it wrong.\nInstead of making what they want, they try to make what some\nimaginary, more sophisticated audience wants. And once you go down\nthat route, you're lost.\n[6]

There are a lot of forces that will lead you astray when you're\ntrying to figure out what to work on. Pretentiousness, fashion,\nfear, money, politics, other people's wishes, eminent frauds. But\nif you stick to what you find genuinely interesting, you'll be proof\nagainst all of them. If you're interested, you're not astray.

\nFollowing your interests may sound like a rather passive strategy,\nbut in practice it usually means following them past all sorts of\nobstacles. You usually have to risk rejection and failure. So it\ndoes take a good deal of boldness.

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

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

I think for most people who want to do great work, the right strategy\nis not to plan too much. At each stage do whatever seems most\ninteresting and gives you the best options for the future. I call\nthis approach \"staying upwind.\" This is how most people who've done\ngreat work seem to have done it.

\nEven when you've found something exciting to work on, working on\nit is not always straightforward. There will be times when some new\nidea makes you leap out of bed in the morning and get straight to\nwork. But there will also be plenty of times when things aren't\nlike that.

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

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

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

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

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

Similar techniques work for starting new projects. It's ok to lie\nto yourself about how much work a project will entail, for example.\nLots of great things began with someone saying \"How hard could it\nbe?\"

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

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

Another permissible lie is to exaggerate the importance of what\nyou're working on, at least in your own mind. If that helps you\ndiscover something new, it may turn out not to have been a lie after\nall.\n[7]

\nSince there are two senses of starting work — per day and per\nproject — there are also two forms of procrastination. Per-project\nprocrastination is far the more dangerous. You put off starting\nthat ambitious project from year to year because the time isn't\nquite right. When you're procrastinating in units of years, you can\nget a lot not done.\n[8]

One reason per-project procrastination is so dangerous is that it\nusually camouflages itself as work. You're not just sitting around\ndoing nothing; you're working industriously on something else. So\nper-project procrastination doesn't set off the alarms that per-day\nprocrastination does. You're too busy to notice it.

The way to beat it is to stop occasionally and ask yourself: Am I\nworking on what I most want to work on? When you're young it's ok\nif the answer is sometimes no, but this gets increasingly dangerous\nas you get older.\n[9]

\nGreat work usually entails spending what would seem to most people\nan unreasonable amount of time on a problem. You can't think of\nthis time as a cost, or it will seem too high. You have to find the\nwork sufficiently engaging as it's happening.

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

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

If you do work that compounds, you'll get exponential growth. Most\npeople who do this do it unconsciously, but it's worth stopping to\nthink about. Learning, for example, is an instance of this phenomenon:\nthe more you learn about something, the easier it is to learn more.\nGrowing an audience is another: the more fans you have, the more\nnew fans they'll bring you.

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

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

\nWork doesn't just happen when you're trying to. There's a kind of\nundirected thinking you do when walking or taking a shower or lying\nin bed that can be very powerful. By letting your mind wander a\nlittle, you'll often solve problems you were unable to solve by\nfrontal attack.

You have to be working hard in the normal way to benefit from this\nphenomenon, though. You can't just walk around daydreaming. The\ndaydreaming has to be interleaved with deliberate work that feeds\nit questions.\n[10]

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

\nConsciously cultivate your taste in the work done in your field.\nUntil you know which is the best and what makes it so, you don't\nknow what you're aiming for.

And that is what you're aiming for, because if you don't try to\nbe the best, you won't even be good. This observation has been made\nby so many people in so many different fields that it might be worth\nthinking about why it's true. It could be because ambition is a\nphenomenon where almost all the error is in one direction — where\nalmost all the shells that miss the target miss by falling short.\nOr it could be because ambition to be the best is a qualitatively\ndifferent thing from ambition to be good. Or maybe being good is\nsimply too vague a standard. Probably all three are true.\n[11]

Fortunately there's a kind of economy of scale here. Though it might\nseem like you'd be taking on a heavy burden by trying to be the\nbest, in practice you often end up net ahead. It's exciting, and\nalso strangely liberating. It simplifies things. In some ways it's\neasier to try to be the best than to try merely to be good.

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

\nDon't try to work in a distinctive style. Just try to do the best\njob you can; you won't be able to help doing it in a distinctive\nway.

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

Affectation is in effect to pretend that someone other than you is\ndoing the work. You adopt an impressive but fake persona, and while\nyou're pleased with the impressiveness, the fakeness is what shows\nin the work.\n[12]

The temptation to be someone else is greatest for the young. They\noften feel like nobodies. But you never need to worry about that\nproblem, because it's self-solving if you work on sufficiently\nambitious projects. If you succeed at an ambitious project, you're\nnot a nobody; you're the person who did it. So just do the work and\nyour identity will take care of itself.

\n\"Avoid affectation\" is a useful rule so far as it goes, but how\nwould you express this idea positively? How would you say what to\nbe, instead of what not to be? The best answer is earnest. If you're\nearnest you avoid not just affectation but a whole set of similar\nvices.

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

One way to avoid intellectual dishonesty is to maintain a slight\npositive pressure in the opposite direction. Be aggressively willing\nto admit that you're mistaken. Once you've admitted you were mistaken\nabout something, you're free. Till then you have to carry it.\n[13]

Another more subtle component of earnestness is informality.\nInformality is much more important than its grammatically negative\nname implies. It's not merely the absence of something. It means\nfocusing on what matters instead of what doesn't.

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

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

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

Some people are naturally earnest, and with others it takes a\nconscious effort. Either kind of earnestness will suffice. But I\ndoubt it would be possible to do great work without being earnest.\nIt's so hard to do even if you are. You don't have enough margin\nfor error to accommodate the distortions introduced by being affected,\nintellectually dishonest, orthodox, fashionable, or cool.\n[14]

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

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

Have the confidence to cut. Don't keep something that doesn't fit\njust because you're proud of it, or because it cost you a lot of\neffort.

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

Mathematical elegance may sound like a mere metaphor, drawn from\nthe arts. That's what I thought when I first heard the term \"elegant\"\napplied to a proof. But now I suspect it's conceptually prior — \nthat the main ingredient in artistic elegance is mathematical\nelegance. At any rate it's a useful standard well beyond math.

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

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

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

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

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

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

If you express your ideas in the most general form, they'll be truer\nthan you intended.

\nTrue by itself is not enough, of course. Great ideas have to be\ntrue and new. And it takes a certain amount of ability to see new\nideas even once you've learned enough to get to one of the frontiers\nof knowledge.

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

I've never liked the term \"creative process.\" It seems misleading.\nOriginality isn't a process, but a habit of mind. Original thinkers\nthrow off new ideas about whatever they focus on, like an angle\ngrinder throwing off sparks. They can't help it.

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

I don't know if it's possible to cultivate originality, but there\nare definitely ways to make the most of however much you have. For\nexample, you're much more likely to have original ideas when you're\nworking on something. Original ideas don't come from trying to have\noriginal ideas. They come from trying to build or understand something\nslightly too difficult.\n[15]

Talking or writing about the things you're interested in is a good\nway to generate new ideas. When you try to put ideas into words, a\nmissing idea creates a sort of vacuum that draws it out of you.\nIndeed, there's a kind of thinking that can only be done by writing.

Changing your context can help. If you visit a new place, you'll\noften find you have new ideas there. The journey itself often\ndislodges them. But you may not have to go far to get this benefit.\nSometimes it's enough just to go for a walk.\n[16]

It also helps to travel in topic space. You'll have more new ideas\nif you explore lots of different topics, partly because it gives\nthe angle grinder more surface area to work on, and partly because\nanalogies are an especially fruitful source of new ideas.

Don't divide your attention evenly between many topics though,\nor you'll spread yourself too thin. You want to distribute it\naccording to something more like a power law.\n[17]\nBe professionally\ncurious about a few topics and idly curious about many more.

Curiosity and originality are closely related. Curiosity feeds\noriginality by giving it new things to work on. But the relationship\nis closer than that. Curiosity is itself a kind of originality;\nit's roughly to questions what originality is to answers. And since\nquestions at their best are a big component of answers, curiosity\nat its best is a creative force.

\nHaving new ideas is a strange game, because it usually consists of\nseeing things that were right under your nose. Once you've seen a\nnew idea, it tends to seem obvious. Why did no one think of this\nbefore?

When an idea seems simultaneously novel and obvious, it's probably\na good one.

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

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

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

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

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

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

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

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

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

Strictness plus rule-breaking sounds like a strange combination.\nIn popular culture they're opposed. But popular culture has a broken\nmodel in this respect. It implicitly assumes that issues are trivial\nones, and in trivial matters strictness and rule-breaking are\nopposed. But in questions that really matter, only rule-breakers\ncan be truly strict.

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

One way to do that is to ask what would be good ideas for someone\nelse to explore. Then your subconscious won't shoot them down to\nprotect you.

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

Religions are collections of cherished but mistaken principles. So\nanything that can be described either literally or metaphorically\nas a religion will have valuable unexplored ideas in its shadow.\nCopernicus and Darwin both made discoveries of this type.\n[18]

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

\nPeople show much more originality in solving problems than in\ndeciding which problems to solve. Even the smartest can be surprisingly\nconservative when deciding what to work on. People who'd never dream\nof being fashionable in any other way get sucked into working on\nfashionable problems.

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

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

Working on an unfashionable problem can be very pleasing. There's\nno hype or hurry. Opportunists and critics are both occupied\nelsewhere. The existing work often has an old-school solidity. And\nthere's a satisfying sense of economy in cultivating ideas that\nwould otherwise be wasted.

But the most common type of overlooked problem is not explicitly\nunfashionable in the sense of being out of fashion. It just doesn't\nseem to matter as much as it actually does. How do you find these?\nBy being self-indulgent — by letting your curiosity have its way,\nand tuning out, at least temporarily, the little voice in your head\nthat says you should only be working on \"important\" problems.

You do need to work on important problems, but almost everyone is\ntoo conservative about what counts as one. And if there's an important\nbut overlooked problem in your neighborhood, it's probably already\non your subconscious radar screen. So try asking yourself: if you\nwere going to take a break from \"serious\" work to work on something\njust because it would be really interesting, what would you do? The\nanswer is probably more important than it seems.

Originality in choosing problems seems to matter even more than\noriginality in solving them. That's what distinguishes the people\nwho discover whole new fields. So what might seem to be merely the\ninitial step — deciding what to work on — is in a sense the key\nto the whole game.

\nFew grasp this. One of the biggest misconceptions about new ideas\nis about the ratio of question to answer in their composition.\nPeople think big ideas are answers, but often the real insight was\nin the question.

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

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

Sometimes you carry a question for a long time. Great work often\ncomes from returning to a question you first noticed years before\n— in your childhood, even — and couldn't stop thinking about.\nPeople talk a lot about the importance of keeping your youthful\ndreams alive, but it's just as important to keep your youthful\nquestions alive.\n[19]

This is one of the places where actual expertise differs most from\nthe popular picture of it. In the popular picture, experts are\ncertain. But actually the more puzzled you are, the better, so long\nas (a) the things you're puzzled about matter, and (b) no one else\nunderstands them either.

Think about what's happening at the moment just before a new idea\nis discovered. Often someone with sufficient expertise is puzzled\nabout something. Which means that originality consists partly of\npuzzlement — of confusion! You have to be comfortable enough with\nthe world being full of puzzles that you're willing to see them,\nbut not so comfortable that you don't want to solve them.\n[20]

It's a great thing to be rich in unanswered questions. And this is\none of those situations where the rich get richer, because the best\nway to acquire new questions is to try answering existing ones.\nQuestions don't just lead to answers, but also to more questions.

\nThe best questions grow in the answering. You notice a thread\nprotruding from the current paradigm and try pulling on it, and it\njust gets longer and longer. So don't require a question to be\nobviously big before you try answering it. You can rarely predict\nthat. It's hard enough even to notice the thread, let alone to\npredict how much will unravel if you pull on it.

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

Being prolific is underrated. The more different things you try,\nthe greater the chance of discovering something new. Understand,\nthough, that trying lots of things will mean trying lots of things\nthat don't work. You can't have a lot of good ideas without also\nhaving a lot of bad ones.\n[21]

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

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

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

Begin by trying the simplest thing that could possibly work.\nSurprisingly often, it does. If it doesn't, this will at least get\nyou started.

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

An early version of a new project will sometimes be dismissed as a\ntoy. It's a good sign when people do this. That means it has\neverything a new idea needs except scale, and that tends to follow.\n[22]

The alternative to starting with something small and evolving it\nis to plan in advance what you're going to do. And planning does\nusually seem the more responsible choice. It sounds more organized\nto say \"we're going to do x and then y and then z\" than \"we're going\nto try x and see what happens.\" And it is more organized; it just\ndoesn't work as well.

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

\nTake as much risk as you can afford. In an efficient market, risk\nis proportionate to reward, so don't look for certainty, but for a\nbet with high expected value. If you're not failing occasionally,\nyou're probably being too conservative.

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

Even a project that fails can be valuable. In the process of working\non it, you'll have crossed territory few others have seen, and\nencountered questions few others have asked. And there's probably\nno better source of questions than the ones you encounter in trying\nto do something slightly too hard.

\nUse the advantages of youth when you have them, and the advantages\nof age once you have those. The advantages of youth are energy,\ntime, optimism, and freedom. The advantages of age are knowledge,\nefficiency, money, and power. With effort you can acquire some of\nthe latter when young and keep some of the former when old.

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

That \"slightly\" is an important qualification. Spend time lavishly\nwhen you're young, but don't simply waste it. There's a big difference\nbetween doing something you worry might be a waste of time and doing\nsomething you know for sure will be. The former is at least a bet,\nand possibly a better one than you think.\n[23]

The most subtle advantage of youth, or more precisely of inexperience,\nis that you're seeing everything with fresh eyes. When your brain\nembraces an idea for the first time, sometimes the two don't fit\ntogether perfectly. Usually the problem is with your brain, but\noccasionally it's with the idea. A piece of it sticks out awkwardly\nand jabs you when you think about it. People who are used to the\nidea have learned to ignore it, but you have the opportunity not\nto.\n[24]

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

\nOne of the most valuable kinds of knowledge you get from experience\nis to know what you don't have to worry about. The young know all\nthe things that could matter, but not their relative importance.\nSo they worry equally about everything, when they should worry much\nmore about a few things and hardly at all about the rest.

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

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

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

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

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

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

\nDon't think of yourself as dependent on some gatekeeper giving you\na \"big break.\" Even if this were true, the best way to get it would\nbe to focus on doing good work rather than chasing influential\npeople.

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

\nPeople new to a field will often copy existing work. There's nothing\ninherently bad about that. There's no better way to learn how\nsomething works than by trying to reproduce it. Nor does\ncopying necessarily make your work unoriginal. Originality is the\npresence of new ideas, not the absence of old ones.

There's a good way to copy and a bad way. If you're going to copy\nsomething, do it openly instead of furtively, or worse still,\nunconsciously. This is what's meant by the famously misattributed\nphrase \"Great artists steal.\" The really dangerous kind of copying,\nthe kind that gives copying a bad name, is the kind that's done\nwithout realizing it, because you're nothing more than a train\nrunning on tracks laid down by someone else. But at the other\nextreme, copying can be a sign of superiority rather than subordination.\n[25]

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

Oddly enough, the very novelty of the most novel ideas sometimes\nmakes them seem at first to be more derivative than they are. New\ndiscoveries often have to be conceived initially as variations of\nexisting things, even by their discoverers, because there isn't\nyet the conceptual vocabulary to express them.

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

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

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

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

One of the most powerful kinds of copying is to copy something from\none field into another. History is so full of chance discoveries\nof this type that it's probably worth giving chance a hand by\ndeliberately learning about other kinds of work. You can take ideas\nfrom quite distant fields if you let them be metaphors.

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

\nIf a lot of the best people in your field are collected in one\nplace, it's usually a good idea to visit for a while. It will\nincrease your ambition, and also, by showing you that these people\nare human, increase your self-confidence.\n[26]

If you're earnest you'll probably get a warmer welcome than you\nmight expect. Most people who are very good at something are happy\nto talk about it with anyone who's genuinely interested. If they're\nreally good at their work, then they probably have a hobbyist's\ninterest in it, and hobbyists always want to talk about their\nhobbies.

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

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

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

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

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

Most of us can benefit from collaborating with colleagues, but some\nprojects require people on a larger scale, and starting one of those\nis not for everyone. If you want to run a project like that, you'll\nhave to become a manager, and managing well takes aptitude and\ninterest like any other kind of work. If you don't have them, there\nis no middle path: you must either force yourself to learn management\nas a second language, or avoid such projects.\n[27]

\nHusband your morale. It's the basis of everything when you're working\non ambitious projects. You have to nurture and protect it like a\nliving organism.

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

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

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

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

Doing great work is a depth-first search whose root node is the\ndesire to. So \"If at first you don't succeed, try, try again\" isn't\nquite right. It should be: If at first you don't succeed, either\ntry again, or backtrack and then try again.

\"Never give up\" is also not quite right. Obviously there are times\nwhen it's the right choice to eject. A more precise version would\nbe: Never let setbacks panic you into backtracking more than you\nneed to. Corollary: Never abandon the root node.

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

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

To the extent you can, avoid letting intermediaries come between\nyou and your audience. In some types of work this is inevitable,\nbut it's so liberating to escape it that you might be better off\nswitching to an adjacent type if that will let you go direct.\n[28]

The people you spend time with will also have a big effect on your\nmorale. You'll find there are some who increase your energy and\nothers who decrease it, and the effect someone has is not always\nwhat you'd expect. Seek out the people who increase your energy and\navoid those who decrease it. Though of course if there's someone\nyou need to take care of, that takes precedence.

Don't marry someone who doesn't understand that you need to work,\nor sees your work as competition for your attention. If you're\nambitious, you need to work; it's almost like a medical condition;\nso someone who won't let you work either doesn't understand you,\nor does and doesn't care.

Ultimately morale is physical. You think with your body, so it's\nimportant to take care of it. That means exercising regularly,\neating and sleeping well, and avoiding the more dangerous kinds of\ndrugs. Running and walking are particularly good forms of exercise\nbecause they're good for thinking.\n[29]

People who do great work are not necessarily happier than everyone\nelse, but they're happier than they'd be if they didn't. In fact,\nif you're smart and ambitious, it's dangerous not to be productive.\nPeople who are smart and ambitious but don't achieve much tend to\nbecome bitter.

\nIt's ok to want to impress other people, but choose the right people.\nThe opinion of people you respect is signal. Fame, which is the\nopinion of a much larger group you might or might not respect, just\nadds noise.

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

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

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

\nNotice how often that word has come up. If you asked an oracle the\nsecret to doing great work and the oracle replied with a single\nword, my bet would be on \"curiosity.\"

That doesn't translate directly to advice. It's not enough just to\nbe curious, and you can't command curiosity anyway. But you can\nnurture it and let it drive you.

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

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

The factors in doing great work are factors in the literal,\nmathematical sense, and they are: ability, interest, effort, and\nluck. Luck by definition you can't do anything about, so we can\nignore that. And we can assume effort, if you do in fact want to\ndo great work. So the problem boils down to ability and interest.\nCan you find a kind of work where your ability and interest will\ncombine to yield an explosion of new ideas?

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

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

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

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

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

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

Notes

[1]\nI don't think you could give a precise definition of what\ncounts as great work. Doing great work means doing something important\nso well that you expand people's ideas of what's possible. But\nthere's no threshold for importance. It's a matter of degree, and\noften hard to judge at the time anyway. So I'd rather people focused\non developing their interests rather than worrying about whether\nthey're important or not. Just try to do something amazing, and\nleave it to future generations to say if you succeeded.

[2]\nA lot of standup comedy is based on noticing anomalies in\neveryday life. \"Did you ever notice...?\" New ideas come from doing\nthis about nontrivial things. Which may help explain why people's\nreaction to a new idea is often the first half of laughing: Ha!

[3]\nThat second qualifier is critical. If you're excited about\nsomething most authorities discount, but you can't give a more\nprecise explanation than \"they don't get it,\" then you're starting\nto drift into the territory of cranks.

[4]\nFinding something to work on is not simply a matter of finding\na match between the current version of you and a list of known\nproblems. You'll often have to coevolve with the problem. That's\nwhy it can sometimes be so hard to figure out what to work on. The\nsearch space is huge. It's the cartesian product of all possible\ntypes of work, both known and yet to be discovered, and all possible\nfuture versions of you.

There's no way you could search this whole space, so you have to\nrely on heuristics to generate promising paths through it and hope\nthe best matches will be clustered. Which they will not always be;\ndifferent types of work have been collected together as much by\naccidents of history as by the intrinsic similarities between them.

[5]\nThere are many reasons curious people are more likely to do\ngreat work, but one of the more subtle is that, by casting a wide\nnet, they're more likely to find the right thing to work on in the\nfirst place.

[6]\nIt can also be dangerous to make things for an audience you\nfeel is less sophisticated than you, if that causes you to talk\ndown to them. You can make a lot of money doing that, if you do it\nin a sufficiently cynical way, but it's not the route to great work.\nNot that anyone using this m.o. would care.

[7]\nThis idea I learned from Hardy's A Mathematician's Apology,\nwhich I recommend to anyone ambitious to do great work, in any\nfield.

[8]\nJust as we overestimate what we can do in a day and underestimate\nwhat we can do over several years, we overestimate the damage done\nby procrastinating for a day and underestimate the damage done by\nprocrastinating for several years.

[9]\nYou can't usually get paid for doing exactly what you want,\nespecially early on. There are two options: get paid for doing work\nclose to what you want and hope to push it closer, or get paid for\ndoing something else entirely and do your own projects on the side.\nBoth can work, but both have drawbacks: in the first approach your\nwork is compromised by default, and in the second you have to fight\nto get time to do it.

[10]\nIf you set your life up right, it will deliver the focus-relax\ncycle automatically. The perfect setup is an office you work in and\nthat you walk to and from.

[11]\nThere may be some very unworldly people who do great work\nwithout consciously trying to. If you want to expand this rule to\ncover that case, it becomes: Don't try to be anything except the\nbest.

[12]\nThis gets more complicated in work like acting, where the\ngoal is to adopt a fake persona. But even here it's possible to be\naffected. Perhaps the rule in such fields should be to avoid\nunintentional affectation.

[13]\nIt's safe to have beliefs that you treat as unquestionable\nif and only if they're also unfalsifiable. For example, it's safe\nto have the principle that everyone should be treated equally under\nthe law, because a sentence with a \"should\" in it isn't really a\nstatement about the world and is therefore hard to disprove. And\nif there's no evidence that could disprove one of your principles,\nthere can't be any facts you'd need to ignore in order to preserve\nit.

[14]\nAffectation is easier to cure than intellectual dishonesty.\nAffectation is often a shortcoming of the young that burns off in\ntime, while intellectual dishonesty is more of a character flaw.

[15]\nObviously you don't have to be working at the exact moment\nyou have the idea, but you'll probably have been working fairly\nrecently.

[16]\nSome say psychoactive drugs have a similar effect. I'm\nskeptical, but also almost totally ignorant of their effects.

[17]\nFor example you might give the nth most important topic\n(m-1)/m^n of your attention, for some m > 1. You couldn't allocate\nyour attention so precisely, of course, but this at least gives an\nidea of a reasonable distribution.

[18]\nThe principles defining a religion have to be mistaken.\nOtherwise anyone might adopt them, and there would be nothing to\ndistinguish the adherents of the religion from everyone else.

[19]\nIt might be a good exercise to try writing down a list of\nquestions you wondered about in your youth. You might find you're\nnow in a position to do something about some of them.

[20]\nThe connection between originality and uncertainty causes a\nstrange phenomenon: because the conventional-minded are more certain\nthan the independent-minded, this tends to give them the upper hand\nin disputes, even though they're generally stupider.\n
\n The best lack all conviction, while the worst
\n Are full of passionate intensity.\n
\n[21]\nDerived from Linus Pauling's \"If you want to have good ideas,\nyou must have many ideas.\"

[22]\nAttacking a project as a \"toy\" is similar to attacking a\nstatement as \"inappropriate.\" It means that no more substantial\ncriticism can be made to stick.

[23]\nOne way to tell whether you're wasting time is to ask if\nyou're producing or consuming. Writing computer games is less likely\nto be a waste of time than playing them, and playing games where\nyou create something is less likely to be a waste of time than\nplaying games where you don't.

[24]\nAnother related advantage is that if you haven't said anything\npublicly yet, you won't be biased toward evidence that supports\nyour earlier conclusions. With sufficient integrity you could achieve\neternal youth in this respect, but few manage to. For most people,\nhaving previously published opinions has an effect similar to\nideology, just in quantity 1.

[25]\nIn the early 1630s Daniel Mytens made a painting of Henrietta\nMaria handing a laurel wreath to Charles I. Van Dyck then painted\nhis own version to show how much better he was.

[26]\nI'm being deliberately vague about what a place is. As of\nthis writing, being in the same physical place has advantages that\nare hard to duplicate, but that could change.

[27]\nThis is false when the work the other people have to do is\nvery constrained, as with SETI@home or Bitcoin. It may be possible\nto expand the area in which it's false by defining similarly\nrestricted protocols with more freedom of action in the nodes.

[28]\nCorollary: Building something that enables people to go around\nintermediaries and engage directly with their audience is probably\na good idea.

[29]\nIt may be helpful always to walk or run the same route, because\nthat frees attention for thinking. It feels that way to me, and\nthere is some historical evidence for it.
","textContent":"July 2023\n\nIf you collected lists of techniques for doing great work in a lot\nof different fields, what would the intersection look like? I decided\nto find out by making it.\n\nPartly my goal was to create a guide that could be used by someone\nworking in any field. But I was also curious about the shape of the\nintersection. And one thing this exercise shows is that it does\nhave a definite shape; it's not just a point labelled \"work hard.\"\n\nThe following recipe assumes you're very ambitious.\n\nThe first step is to decide what to work on. The work you choose\nneeds to have three qualities: it has to be something you have a\nnatural aptitude for, that you have a deep interest in, and that\noffers scope to do great work.\n\nIn practice you don't have to worry much about the third criterion.\nAmbitious people are if anything already too conservative about it.\nSo all you need to do is find something you have an aptitude for\nand great interest in.\n[1]\n\nThat sounds straightforward, but it's often quite difficult. When\nyou're young you don't know what you're good at or what different\nkinds of work are like. Some kinds of work you end up doing may not\neven exist yet. So while some people know what they want to do at\n14, most have to figure it out.\n\nThe way to figure out what to work on is by working. If you're not\nsure what to work on, guess. But pick something and get going.\nYou'll probably guess wrong some of the time, but that's fine. It's\ngood to know about multiple things; some of the biggest discoveries\ncome from noticing connections between different fields.\n\nDevelop a habit of working on your own projects. Don't let \"work\"\nmean something other people tell you to do. If you do manage to do\ngreat work one day, it will probably be on a project of your own.\nIt may be within some bigger project, but you'll be driving your\npart of it.\n\nWhat should your projects be? Whatever seems to you excitingly\nambitious. As you grow older and your taste in projects evolves,\nexciting and important will converge. At 7 it may seem excitingly\nambitious to build huge things out of Lego, then at 14 to teach\nyourself calculus, till at 21 you're starting to explore unanswered\nquestions in physics. But always preserve excitingness.\n\nThere's a kind of excited curiosity that's both the engine and the\nrudder of great work. It will not only drive you, but if you let\nit have its way, will also show you what to work on.\n\nWhat are you excessively curious about — curious to a degree that\nwould bore most other people? That's what you're looking for.\n\nOnce you've found something you're excessively interested in, the\nnext step is to learn enough about it to get you to one of the\nfrontiers of knowledge. Knowledge expands fractally, and from a\ndistance its edges look smooth, but once you learn enough to get\nclose to one, they turn out to be full of gaps.\n\nThe next step is to notice them. This takes some skill, because\nyour brain wants to ignore such gaps in order to make a simpler\nmodel of the world. Many discoveries have come from asking questions\nabout things that everyone else took for granted. \n[2]\n\nIf the answers seem strange, so much the better. Great work often\nhas a tincture of strangeness. You see this from painting to math.\nIt would be affected to try to manufacture it, but if it appears,\nembrace it.\n\nBoldly chase outlier ideas, even if other people aren't interested\nin them — in fact, especially if they aren't. If you're excited\nabout some possibility that everyone else ignores, and you have\nenough expertise to say precisely what they're all overlooking,\nthat's as good a bet as you'll find.\n[3]\n\nFour steps: choose a field, learn enough to get to the frontier,\nnotice gaps, explore promising ones. This is how practically everyone\nwho's done great work has done it, from painters to physicists.\n\nSteps two and four will require hard work. It may not be possible\nto prove that you have to work hard to do great things, but the\nempirical evidence is on the scale of the evidence for mortality.\nThat's why it's essential to work on something you're deeply\ninterested in. Interest will drive you to work harder than mere\ndiligence ever could.\n\nThe three most powerful motives are curiosity, delight, and the\ndesire to do something impressive. Sometimes they converge, and\nthat combination is the most powerful of all.\n\nThe big prize is to discover a new fractal bud. You notice a crack\nin the surface of knowledge, pry it open, and there's a whole world\ninside.\n\nLet's talk a little more about the complicated business of figuring\nout what to work on. The main reason it's hard is that you can't\ntell what most kinds of work are like except by doing them. Which\nmeans the four steps overlap: you may have to work at something for\nyears before you know how much you like it or how good you are at\nit. And in the meantime you're not doing, and thus not learning\nabout, most other kinds of work. So in the worst case you choose\nlate based on very incomplete information.\n[4]\n\nThe nature of ambition exacerbates this problem. Ambition comes in\ntwo forms, one that precedes interest in the subject and one that\ngrows out of it. Most people who do great work have a mix, and the\nmore you have of the former, the harder it will be to decide what\nto do.\n\nThe educational systems in most countries pretend it's easy. They\nexpect you to commit to a field long before you could know what\nit's really like. And as a result an ambitious person on an optimal\ntrajectory will often read to the system as an instance of breakage.\n\nIt would be better if they at least admitted it — if they admitted\nthat the system not only can't do much to help you figure out what\nto work on, but is designed on the assumption that you'll somehow\nmagically guess as a teenager. They don't tell you, but I will:\nwhen it comes to figuring out what to work on, you're on your own.\nSome people get lucky and do guess correctly, but the rest will\nfind themselves scrambling diagonally across tracks laid down on\nthe assumption that everyone does.\n\nWhat should you do if you're young and ambitious but don't know\nwhat to work on? What you should not do is drift along passively,\nassuming the problem will solve itself. You need to take action.\nBut there is no systematic procedure you can follow. When you read\nbiographies of people who've done great work, it's remarkable how\nmuch luck is involved. They discover what to work on as a result\nof a chance meeting, or by reading a book they happen to pick up.\nSo you need to make yourself a big target for luck, and the way to\ndo that is to be curious. Try lots of things, meet lots of people,\nread lots of books, ask lots of questions.\n[5]\n\nWhen in doubt, optimize for interestingness. Fields change as you\nlearn more about them. What mathematicians do, for example, is very\ndifferent from what you do in high school math classes. So you need\nto give different types of work a chance to show you what they're\nlike. But a field should become increasingly interesting as you\nlearn more about it. If it doesn't, it's probably not for you.\n\nDon't worry if you find you're interested in different things than\nother people. The stranger your tastes in interestingness, the\nbetter. Strange tastes are often strong ones, and a strong taste\nfor work means you'll be productive. And you're more likely to find\nnew things if you're looking where few have looked before.\n\nOne sign that you're suited for some kind of work is when you like\neven the parts that other people find tedious or frightening.\n\nBut fields aren't people; you don't owe them any loyalty. If in the\ncourse of working on one thing you discover another that's more\nexciting, don't be afraid to switch.\n\nIf you're making something for people, make sure it's something\nthey actually want. The best way to do this is to make something\nyou yourself want. Write the story you want to read; build the tool\nyou want to use. Since your friends probably have similar interests,\nthis will also get you your initial audience.\n\nThis should follow from the excitingness rule. Obviously the most\nexciting story to write will be the one you want to read. The reason\nI mention this case explicitly is that so many people get it wrong.\nInstead of making what they want, they try to make what some\nimaginary, more sophisticated audience wants. And once you go down\nthat route, you're lost.\n[6]\n\nThere are a lot of forces that will lead you astray when you're\ntrying to figure out what to work on. Pretentiousness, fashion,\nfear, money, politics, other people's wishes, eminent frauds. But\nif you stick to what you find genuinely interesting, you'll be proof\nagainst all of them. If you're interested, you're not astray.\n\nFollowing your interests may sound like a rather passive strategy,\nbut in practice it usually means following them past all sorts of\nobstacles. You usually have to risk rejection and failure. So it\ndoes take a good deal of boldness.\n\nBut while you need boldness, you don't usually need much planning.\nIn most cases the recipe for doing great work is simply: work hard\non excitingly ambitious projects, and something good will come of\nit. Instead of making a plan and then executing it, you just try\nto preserve certain invariants.\n\nThe trouble with planning is that it only works for achievements\nyou can describe in advance. You can win a gold medal or get rich\nby deciding to as a child and then tenaciously pursuing that goal,\nbut you can't discover natural selection that way.\n\nI think for most people who want to do great work, the right strategy\nis not to plan too much. At each stage do whatever seems most\ninteresting and gives you the best options for the future. I call\nthis approach \"staying upwind.\" This is how most people who've done\ngreat work seem to have done it.\n\nEven when you've found something exciting to work on, working on\nit is not always straightforward. There will be times when some new\nidea makes you leap out of bed in the morning and get straight to\nwork. But there will also be plenty of times when things aren't\nlike that.\n\nYou don't just put out your sail and get blown forward by inspiration.\nThere are headwinds and currents and hidden shoals. So there's a\ntechnique to working, just as there is to sailing.\n\nFor example, while you must work hard, it's possible to work too\nhard, and if you do that you'll find you get diminishing returns:\nfatigue will make you stupid, and eventually even damage your health.\nThe point at which work yields diminishing returns depends on the\ntype. Some of the hardest types you might only be able to do for\nfour or five hours a day.\n\nIdeally those hours will be contiguous. To the extent you can, try\nto arrange your life so you have big blocks of time to work in.\nYou'll shy away from hard tasks if you know you might be interrupted.\n\nIt will probably be harder to start working than to keep working.\nYou'll often have to trick yourself to get over that initial\nthreshold. Don't worry about this; it's the nature of work, not a\nflaw in your character. Work has a sort of activation energy, both\nper day and per project. And since this threshold is fake in the\nsense that it's higher than the energy required to keep going, it's\nok to tell yourself a lie of corresponding magnitude to get over\nit.\n\nIt's usually a mistake to lie to yourself if you want to do great\nwork, but this is one of the rare cases where it isn't. When I'm\nreluctant to start work in the morning, I often trick myself by\nsaying \"I'll just read over what I've got so far.\" Five minutes\nlater I've found something that seems mistaken or incomplete, and\nI'm off.\n\nSimilar techniques work for starting new projects. It's ok to lie\nto yourself about how much work a project will entail, for example.\nLots of great things began with someone saying \"How hard could it\nbe?\"\n\nThis is one case where the young have an advantage. They're more\noptimistic, and even though one of the sources of their optimism\nis ignorance, in this case ignorance can sometimes beat knowledge.\n\nTry to finish what you start, though, even if it turns out to be\nmore work than you expected. Finishing things is not just an exercise\nin tidiness or self-discipline. In many projects a lot of the best\nwork happens in what was meant to be the final stage.\n\nAnother permissible lie is to exaggerate the importance of what\nyou're working on, at least in your own mind. If that helps you\ndiscover something new, it may turn out not to have been a lie after\nall.\n[7]\n\nSince there are two senses of starting work — per day and per\nproject — there are also two forms of procrastination. Per-project\nprocrastination is far the more dangerous. You put off starting\nthat ambitious project from year to year because the time isn't\nquite right. When you're procrastinating in units of years, you can\nget a lot not done.\n[8]\n\nOne reason per-project procrastination is so dangerous is that it\nusually camouflages itself as work. You're not just sitting around\ndoing nothing; you're working industriously on something else. So\nper-project procrastination doesn't set off the alarms that per-day\nprocrastination does. You're too busy to notice it.\n\nThe way to beat it is to stop occasionally and ask yourself: Am I\nworking on what I most want to work on? When you're young it's ok\nif the answer is sometimes no, but this gets increasingly dangerous\nas you get older.\n[9]\n\nGreat work usually entails spending what would seem to most people\nan unreasonable amount of time on a problem. You can't think of\nthis time as a cost, or it will seem too high. You have to find the\nwork sufficiently engaging as it's happening.\n\nThere may be some jobs where you have to work diligently for years\nat things you hate before you get to the good part, but this is not\nhow great work happens. Great work happens by focusing consistently\non something you're genuinely interested in. When you pause to take\nstock, you're surprised how far you've come.\n\nThe reason we're surprised is that we underestimate the cumulative\neffect of work. Writing a page a day doesn't sound like much, but\nif you do it every day you'll write a book a year. That's the key:\nconsistency. People who do great things don't get a lot done every\nday. They get something done, rather than nothing.\n\nIf you do work that compounds, you'll get exponential growth. Most\npeople who do this do it unconsciously, but it's worth stopping to\nthink about. Learning, for example, is an instance of this phenomenon:\nthe more you learn about something, the easier it is to learn more.\nGrowing an audience is another: the more fans you have, the more\nnew fans they'll bring you.\n\nThe trouble with exponential growth is that the curve feels flat\nin the beginning. It isn't; it's still a wonderful exponential\ncurve. But we can't grasp that intuitively, so we underrate exponential\ngrowth in its early stages.\n\nSomething that grows exponentially can become so valuable that it's\nworth making an extraordinary effort to get it started. But since\nwe underrate exponential growth early on, this too is mostly done\nunconsciously: people push through the initial, unrewarding phase\nof learning something new because they know from experience that\nlearning new things always takes an initial push, or they grow their\naudience one fan at a time because they have nothing better to do.\nIf people consciously realized they could invest in exponential\ngrowth, many more would do it.\n\nWork doesn't just happen when you're trying to. There's a kind of\nundirected thinking you do when walking or taking a shower or lying\nin bed that can be very powerful. By letting your mind wander a\nlittle, you'll often solve problems you were unable to solve by\nfrontal attack.\n\nYou have to be working hard in the normal way to benefit from this\nphenomenon, though. You can't just walk around daydreaming. The\ndaydreaming has to be interleaved with deliberate work that feeds\nit questions.\n[10]\n\nEveryone knows to avoid distractions at work, but it's also important\nto avoid them in the other half of the cycle. When you let your\nmind wander, it wanders to whatever you care about most at that\nmoment. So avoid the kind of distraction that pushes your work out\nof the top spot, or you'll waste this valuable type of thinking on\nthe distraction instead. (Exception: Don't avoid love.)\n\nConsciously cultivate your taste in the work done in your field.\nUntil you know which is the best and what makes it so, you don't\nknow what you're aiming for.\n\nAnd that is what you're aiming for, because if you don't try to\nbe the best, you won't even be good. This observation has been made\nby so many people in so many different fields that it might be worth\nthinking about why it's true. It could be because ambition is a\nphenomenon where almost all the error is in one direction — where\nalmost all the shells that miss the target miss by falling short.\nOr it could be because ambition to be the best is a qualitatively\ndifferent thing from ambition to be good. Or maybe being good is\nsimply too vague a standard. Probably all three are true.\n[11]\n\nFortunately there's a kind of economy of scale here. Though it might\nseem like you'd be taking on a heavy burden by trying to be the\nbest, in practice you often end up net ahead. It's exciting, and\nalso strangely liberating. It simplifies things. In some ways it's\neasier to try to be the best than to try merely to be good.\n\nOne way to aim high is to try to make something that people will\ncare about in a hundred years. Not because their opinions matter\nmore than your contemporaries', but because something that still\nseems good in a hundred years is more likely to be genuinely good.\n\nDon't try to work in a distinctive style. Just try to do the best\njob you can; you won't be able to help doing it in a distinctive\nway.\n\nStyle is doing things in a distinctive way without trying to. Trying\nto is affectation.\n\nAffectation is in effect to pretend that someone other than you is\ndoing the work. You adopt an impressive but fake persona, and while\nyou're pleased with the impressiveness, the fakeness is what shows\nin the work.\n[12]\n\nThe temptation to be someone else is greatest for the young. They\noften feel like nobodies. But you never need to worry about that\nproblem, because it's self-solving if you work on sufficiently\nambitious projects. If you succeed at an ambitious project, you're\nnot a nobody; you're the person who did it. So just do the work and\nyour identity will take care of itself.\n\n\"Avoid affectation\" is a useful rule so far as it goes, but how\nwould you express this idea positively? How would you say what to\nbe, instead of what not to be? The best answer is earnest. If you're\nearnest you avoid not just affectation but a whole set of similar\nvices.\n\nThe core of being earnest is being intellectually honest. We're\ntaught as children to be honest as an unselfish virtue — as a kind\nof sacrifice. But in fact it's a source of power too. To see new\nideas, you need an exceptionally sharp eye for the truth. You're\ntrying to see more truth than others have seen so far. And how can\nyou have a sharp eye for the truth if you're intellectually dishonest?\n\nOne way to avoid intellectual dishonesty is to maintain a slight\npositive pressure in the opposite direction. Be aggressively willing\nto admit that you're mistaken. Once you've admitted you were mistaken\nabout something, you're free. Till then you have to carry it.\n[13]\n\nAnother more subtle component of earnestness is informality.\nInformality is much more important than its grammatically negative\nname implies. It's not merely the absence of something. It means\nfocusing on what matters instead of what doesn't.\n\nWhat formality and affectation have in common is that as well as\ndoing the work, you're trying to seem a certain way as you're doing\nit. But any energy that goes into how you seem comes out of being\ngood. That's one reason nerds have an advantage in doing great work:\nthey expend little effort on seeming anything. In fact that's\nbasically the definition of a nerd.\n\nNerds have a kind of innocent boldness that's exactly what you need\nin doing great work. It's not learned; it's preserved from childhood.\nSo hold onto it. Be the one who puts things out there rather than\nthe one who sits back and offers sophisticated-sounding criticisms\nof them. \"It's easy to criticize\" is true in the most literal sense,\nand the route to great work is never easy.\n\nThere may be some jobs where it's an advantage to be cynical and\npessimistic, but if you want to do great work it's an advantage to\nbe optimistic, even though that means you'll risk looking like a\nfool sometimes. There's an old tradition of doing the opposite. The\nOld Testament says it's better to keep quiet lest you look like a\nfool. But that's advice for seeming smart. If you actually want\nto discover new things, it's better to take the risk of telling\npeople your ideas.\n\nSome people are naturally earnest, and with others it takes a\nconscious effort. Either kind of earnestness will suffice. But I\ndoubt it would be possible to do great work without being earnest.\nIt's so hard to do even if you are. You don't have enough margin\nfor error to accommodate the distortions introduced by being affected,\nintellectually dishonest, orthodox, fashionable, or cool.\n[14]\n\nGreat work is consistent not only with who did it, but with itself.\nIt's usually all of a piece. So if you face a decision in the middle\nof working on something, ask which choice is more consistent.\n\nYou may have to throw things away and redo them. You won't necessarily\nhave to, but you have to be willing to. And that can take some\neffort; when there's something you need to redo, status quo bias\nand laziness will combine to keep you in denial about it. To beat\nthis ask: If I'd already made the change, would I want to revert\nto what I have now?\n\nHave the confidence to cut. Don't keep something that doesn't fit\njust because you're proud of it, or because it cost you a lot of\neffort.\n\nIndeed, in some kinds of work it's good to strip whatever you're\ndoing to its essence. The result will be more concentrated; you'll\nunderstand it better; and you won't be able to lie to yourself about\nwhether there's anything real there.\n\nMathematical elegance may sound like a mere metaphor, drawn from\nthe arts. That's what I thought when I first heard the term \"elegant\"\napplied to a proof. But now I suspect it's conceptually prior — \nthat the main ingredient in artistic elegance is mathematical\nelegance. At any rate it's a useful standard well beyond math.\n\nElegance can be a long-term bet, though. Laborious solutions will\noften have more prestige in the short term. They cost a lot of\neffort and they're hard to understand, both of which impress people,\nat least temporarily.\n\nWhereas some of the very best work will seem like it took comparatively\nlittle effort, because it was in a sense already there. It didn't\nhave to be built, just seen. It's a very good sign when it's hard\nto say whether you're creating something or discovering it.\n\nWhen you're doing work that could be seen as either creation or\ndiscovery, err on the side of discovery. Try thinking of yourself\nas a mere conduit through which the ideas take their natural shape.\n\n(Strangely enough, one exception is the problem of choosing a problem\nto work on. This is usually seen as search, but in the best case\nit's more like creating something. In the best case you create the\nfield in the process of exploring it.)\n\nSimilarly, if you're trying to build a powerful tool, make it\ngratuitously unrestrictive. A powerful tool almost by definition\nwill be used in ways you didn't expect, so err on the side of\neliminating restrictions, even if you don't know what the benefit\nwill be.\n\nGreat work will often be tool-like in the sense of being something\nothers build on. So it's a good sign if you're creating ideas that\nothers could use, or exposing questions that others could answer.\nThe best ideas have implications in many different areas.\n\nIf you express your ideas in the most general form, they'll be truer\nthan you intended.\n\nTrue by itself is not enough, of course. Great ideas have to be\ntrue and new. And it takes a certain amount of ability to see new\nideas even once you've learned enough to get to one of the frontiers\nof knowledge.\n\nIn English we give this ability names like originality, creativity,\nand imagination. And it seems reasonable to give it a separate name,\nbecause it does seem to some extent a separate skill. It's possible\nto have a great deal of ability in other respects — to have a great\ndeal of what's often called technical ability — and yet not have\nmuch of this.\n\nI've never liked the term \"creative process.\" It seems misleading.\nOriginality isn't a process, but a habit of mind. Original thinkers\nthrow off new ideas about whatever they focus on, like an angle\ngrinder throwing off sparks. They can't help it.\n\nIf the thing they're focused on is something they don't understand\nvery well, these new ideas might not be good. One of the most\noriginal thinkers I know decided to focus on dating after he got\ndivorced. He knew roughly as much about dating as the average 15\nyear old, and the results were spectacularly colorful. But to see\noriginality separated from expertise like that made its nature all\nthe more clear.\n\nI don't know if it's possible to cultivate originality, but there\nare definitely ways to make the most of however much you have. For\nexample, you're much more likely to have original ideas when you're\nworking on something. Original ideas don't come from trying to have\noriginal ideas. They come from trying to build or understand something\nslightly too difficult.\n[15]\n\nTalking or writing about the things you're interested in is a good\nway to generate new ideas. When you try to put ideas into words, a\nmissing idea creates a sort of vacuum that draws it out of you.\nIndeed, there's a kind of thinking that can only be done by writing.\n\nChanging your context can help. If you visit a new place, you'll\noften find you have new ideas there. The journey itself often\ndislodges them. But you may not have to go far to get this benefit.\nSometimes it's enough just to go for a walk.\n[16]\n\nIt also helps to travel in topic space. You'll have more new ideas\nif you explore lots of different topics, partly because it gives\nthe angle grinder more surface area to work on, and partly because\nanalogies are an especially fruitful source of new ideas.\n\nDon't divide your attention evenly between many topics though,\nor you'll spread yourself too thin. You want to distribute it\naccording to something more like a power law.\n[17]\nBe professionally\ncurious about a few topics and idly curious about many more.\n\nCuriosity and originality are closely related. Curiosity feeds\noriginality by giving it new things to work on. But the relationship\nis closer than that. Curiosity is itself a kind of originality;\nit's roughly to questions what originality is to answers. And since\nquestions at their best are a big component of answers, curiosity\nat its best is a creative force.\n\nHaving new ideas is a strange game, because it usually consists of\nseeing things that were right under your nose. Once you've seen a\nnew idea, it tends to seem obvious. Why did no one think of this\nbefore?\n\nWhen an idea seems simultaneously novel and obvious, it's probably\na good one.\n\nSeeing something obvious sounds easy. And yet empirically having\nnew ideas is hard. What's the source of this apparent contradiction?\nIt's that seeing the new idea usually requires you to change the\nway you look at the world. We see the world through models that\nboth help and constrain us. When you fix a broken model, new ideas\nbecome obvious. But noticing and fixing a broken model is hard.\nThat's how new ideas can be both obvious and yet hard to discover:\nthey're easy to see after you do something hard.\n\nOne way to discover broken models is to be stricter than other\npeople. Broken models of the world leave a trail of clues where\nthey bash against reality. Most people don't want to see these\nclues. It would be an understatement to say that they're attached\nto their current model; it's what they think in; so they'll tend\nto ignore the trail of clues left by its breakage, however conspicuous\nit may seem in retrospect.\n\nTo find new ideas you have to seize on signs of breakage instead\nof looking away. That's what Einstein did. He was able to see the\nwild implications of Maxwell's equations not so much because he was\nlooking for new ideas as because he was stricter.\n\nThe other thing you need is a willingness to break rules. Paradoxical\nas it sounds, if you want to fix your model of the world, it helps\nto be the sort of person who's comfortable breaking rules. From the\npoint of view of the old model, which everyone including you initially\nshares, the new model usually breaks at least implicit rules.\n\nFew understand the degree of rule-breaking required, because new\nideas seem much more conservative once they succeed. They seem\nperfectly reasonable once you're using the new model of the world\nthey brought with them. But they didn't at the time; it took the\ngreater part of a century for the heliocentric model to be generally\naccepted, even among astronomers, because it felt so wrong.\n\nIndeed, if you think about it, a good new idea has to seem bad to\nmost people, or someone would have already explored it. So what\nyou're looking for is ideas that seem crazy, but the right kind of\ncrazy. How do you recognize these? You can't with certainty. Often\nideas that seem bad are bad. But ideas that are the right kind of\ncrazy tend to be exciting; they're rich in implications; whereas\nideas that are merely bad tend to be depressing.\n\nThere are two ways to be comfortable breaking rules: to enjoy\nbreaking them, and to be indifferent to them. I call these two cases\nbeing aggressively and passively independent-minded.\n\nThe aggressively independent-minded are the naughty ones. Rules\ndon't merely fail to stop them; breaking rules gives them additional\nenergy. For this sort of person, delight at the sheer audacity of\na project sometimes supplies enough activation energy to get it\nstarted.\n\nThe other way to break rules is not to care about them, or perhaps\neven to know they exist. This is why novices and outsiders often\nmake new discoveries; their ignorance of a field's assumptions acts\nas a source of temporary passive independent-mindedness. Aspies\nalso seem to have a kind of immunity to conventional beliefs.\nSeveral I know say that this helps them to have new ideas.\n\nStrictness plus rule-breaking sounds like a strange combination.\nIn popular culture they're opposed. But popular culture has a broken\nmodel in this respect. It implicitly assumes that issues are trivial\nones, and in trivial matters strictness and rule-breaking are\nopposed. But in questions that really matter, only rule-breakers\ncan be truly strict.\n\nAn overlooked idea often doesn't lose till the semifinals. You do\nsee it, subconsciously, but then another part of your subconscious\nshoots it down because it would be too weird, too risky, too much\nwork, too controversial. This suggests an exciting possibility: if\nyou could turn off such filters, you could see more new ideas.\n\nOne way to do that is to ask what would be good ideas for someone\nelse to explore. Then your subconscious won't shoot them down to\nprotect you.\n\nYou could also discover overlooked ideas by working in the other\ndirection: by starting from what's obscuring them. Every cherished\nbut mistaken principle is surrounded by a dead zone of valuable\nideas that are unexplored because they contradict it.\n\nReligions are collections of cherished but mistaken principles. So\nanything that can be described either literally or metaphorically\nas a religion will have valuable unexplored ideas in its shadow.\nCopernicus and Darwin both made discoveries of this type.\n[18]\n\nWhat are people in your field religious about, in the sense of being\ntoo attached to some principle that might not be as self-evident\nas they think? What becomes possible if you discard it?\n\nPeople show much more originality in solving problems than in\ndeciding which problems to solve. Even the smartest can be surprisingly\nconservative when deciding what to work on. People who'd never dream\nof being fashionable in any other way get sucked into working on\nfashionable problems.\n\nOne reason people are more conservative when choosing problems than\nsolutions is that problems are bigger bets. A problem could occupy\nyou for years, while exploring a solution might only take days. But\neven so I think most people are too conservative. They're not merely\nresponding to risk, but to fashion as well. Unfashionable problems\nare undervalued.\n\nOne of the most interesting kinds of unfashionable problem is the\nproblem that people think has been fully explored, but hasn't.\nGreat work often takes something that already exists and shows its\nlatent potential. Durer and Watt both did this. So if you're\ninterested in a field that others think is tapped out, don't let\ntheir skepticism deter you. People are often wrong about this.\n\nWorking on an unfashionable problem can be very pleasing. There's\nno hype or hurry. Opportunists and critics are both occupied\nelsewhere. The existing work often has an old-school solidity. And\nthere's a satisfying sense of economy in cultivating ideas that\nwould otherwise be wasted.\n\nBut the most common type of overlooked problem is not explicitly\nunfashionable in the sense of being out of fashion. It just doesn't\nseem to matter as much as it actually does. How do you find these?\nBy being self-indulgent — by letting your curiosity have its way,\nand tuning out, at least temporarily, the little voice in your head\nthat says you should only be working on \"important\" problems.\n\nYou do need to work on important problems, but almost everyone is\ntoo conservative about what counts as one. And if there's an important\nbut overlooked problem in your neighborhood, it's probably already\non your subconscious radar screen. So try asking yourself: if you\nwere going to take a break from \"serious\" work to work on something\njust because it would be really interesting, what would you do? The\nanswer is probably more important than it seems.\n\nOriginality in choosing problems seems to matter even more than\noriginality in solving them. That's what distinguishes the people\nwho discover whole new fields. So what might seem to be merely the\ninitial step — deciding what to work on — is in a sense the key\nto the whole game.\n\nFew grasp this. One of the biggest misconceptions about new ideas\nis about the ratio of question to answer in their composition.\nPeople think big ideas are answers, but often the real insight was\nin the question.\n\nPart of the reason we underrate questions is the way they're used\nin schools. In schools they tend to exist only briefly before being\nanswered, like unstable particles. But a really good question can\nbe much more than that. A really good question is a partial discovery.\nHow do new species arise? Is the force that makes objects fall to\nearth the same as the one that keeps planets in their orbits? By\neven asking such questions you were already in excitingly novel\nterritory.\n\nUnanswered questions can be uncomfortable things to carry around\nwith you. But the more you're carrying, the greater the chance of\nnoticing a solution — or perhaps even more excitingly, noticing\nthat two unanswered questions are the same.\n\nSometimes you carry a question for a long time. Great work often\ncomes from returning to a question you first noticed years before\n— in your childhood, even — and couldn't stop thinking about.\nPeople talk a lot about the importance of keeping your youthful\ndreams alive, but it's just as important to keep your youthful\nquestions alive.\n[19]\n\nThis is one of the places where actual expertise differs most from\nthe popular picture of it. In the popular picture, experts are\ncertain. But actually the more puzzled you are, the better, so long\nas (a) the things you're puzzled about matter, and (b) no one else\nunderstands them either.\n\nThink about what's happening at the moment just before a new idea\nis discovered. Often someone with sufficient expertise is puzzled\nabout something. Which means that originality consists partly of\npuzzlement — of confusion! You have to be comfortable enough with\nthe world being full of puzzles that you're willing to see them,\nbut not so comfortable that you don't want to solve them.\n[20]\n\nIt's a great thing to be rich in unanswered questions. And this is\none of those situations where the rich get richer, because the best\nway to acquire new questions is to try answering existing ones.\nQuestions don't just lead to answers, but also to more questions.\n\nThe best questions grow in the answering. You notice a thread\nprotruding from the current paradigm and try pulling on it, and it\njust gets longer and longer. So don't require a question to be\nobviously big before you try answering it. You can rarely predict\nthat. It's hard enough even to notice the thread, let alone to\npredict how much will unravel if you pull on it.\n\nIt's better to be promiscuously curious — to pull a little bit on\na lot of threads, and see what happens. Big things start small. The\ninitial versions of big things were often just experiments, or side\nprojects, or talks, which then grew into something bigger. So start\nlots of small things.\n\nBeing prolific is underrated. The more different things you try,\nthe greater the chance of discovering something new. Understand,\nthough, that trying lots of things will mean trying lots of things\nthat don't work. You can't have a lot of good ideas without also\nhaving a lot of bad ones.\n[21]\n\nThough it sounds more responsible to begin by studying everything\nthat's been done before, you'll learn faster and have more fun by\ntrying stuff. And you'll understand previous work better when you\ndo look at it. So err on the side of starting. Which is easier when\nstarting means starting small; those two ideas fit together like\ntwo puzzle pieces.\n\nHow do you get from starting small to doing something great? By\nmaking successive versions. Great things are almost always made in\nsuccessive versions. You start with something small and evolve it,\nand the final version is both cleverer and more ambitious than\nanything you could have planned.\n\nIt's particularly useful to make successive versions when you're\nmaking something for people — to get an initial version in front\nof them quickly, and then evolve it based on their response.\n\nBegin by trying the simplest thing that could possibly work.\nSurprisingly often, it does. If it doesn't, this will at least get\nyou started.\n\nDon't try to cram too much new stuff into any one version. There\nare names for doing this with the first version (taking too long\nto ship) and the second (the second system effect), but these are\nboth merely instances of a more general principle.\n\nAn early version of a new project will sometimes be dismissed as a\ntoy. It's a good sign when people do this. That means it has\neverything a new idea needs except scale, and that tends to follow.\n[22]\n\nThe alternative to starting with something small and evolving it\nis to plan in advance what you're going to do. And planning does\nusually seem the more responsible choice. It sounds more organized\nto say \"we're going to do x and then y and then z\" than \"we're going\nto try x and see what happens.\" And it is more organized; it just\ndoesn't work as well.\n\nPlanning per se isn't good. It's sometimes necessary, but it's a\nnecessary evil — a response to unforgiving conditions. It's something\nyou have to do because you're working with inflexible media, or\nbecause you need to coordinate the efforts of a lot of people. If\nyou keep projects small and use flexible media, you don't have to\nplan as much, and your designs can evolve instead.\n\nTake as much risk as you can afford. In an efficient market, risk\nis proportionate to reward, so don't look for certainty, but for a\nbet with high expected value. If you're not failing occasionally,\nyou're probably being too conservative.\n\nThough conservatism is usually associated with the old, it's the\nyoung who tend to make this mistake. Inexperience makes them fear\nrisk, but it's when you're young that you can afford the most.\n\nEven a project that fails can be valuable. In the process of working\non it, you'll have crossed territory few others have seen, and\nencountered questions few others have asked. And there's probably\nno better source of questions than the ones you encounter in trying\nto do something slightly too hard.\n\nUse the advantages of youth when you have them, and the advantages\nof age once you have those. The advantages of youth are energy,\ntime, optimism, and freedom. The advantages of age are knowledge,\nefficiency, money, and power. With effort you can acquire some of\nthe latter when young and keep some of the former when old.\n\nThe old also have the advantage of knowing which advantages they\nhave. The young often have them without realizing it. The biggest\nis probably time. The young have no idea how rich they are in time.\nThe best way to turn this time to advantage is to use it in slightly\nfrivolous ways: to learn about something you don't need to know\nabout, just out of curiosity, or to try building something just\nbecause it would be cool, or to become freakishly good at something.\n\nThat \"slightly\" is an important qualification. Spend time lavishly\nwhen you're young, but don't simply waste it. There's a big difference\nbetween doing something you worry might be a waste of time and doing\nsomething you know for sure will be. The former is at least a bet,\nand possibly a better one than you think.\n[23]\n\nThe most subtle advantage of youth, or more precisely of inexperience,\nis that you're seeing everything with fresh eyes. When your brain\nembraces an idea for the first time, sometimes the two don't fit\ntogether perfectly. Usually the problem is with your brain, but\noccasionally it's with the idea. A piece of it sticks out awkwardly\nand jabs you when you think about it. People who are used to the\nidea have learned to ignore it, but you have the opportunity not\nto.\n[24]\n\nSo when you're learning about something for the first time, pay\nattention to things that seem wrong or missing. You'll be tempted\nto ignore them, since there's a 99% chance the problem is with you.\nAnd you may have to set aside your misgivings temporarily to keep\nprogressing. But don't forget about them. When you've gotten further\ninto the subject, come back and check if they're still there. If\nthey're still viable in the light of your present knowledge, they\nprobably represent an undiscovered idea.\n\nOne of the most valuable kinds of knowledge you get from experience\nis to know what you don't have to worry about. The young know all\nthe things that could matter, but not their relative importance.\nSo they worry equally about everything, when they should worry much\nmore about a few things and hardly at all about the rest.\n\nBut what you don't know is only half the problem with inexperience.\nThe other half is what you do know that ain't so. You arrive at\nadulthood with your head full of nonsense — bad habits you've\nacquired and false things you've been taught — and you won't be\nable to do great work till you clear away at least the nonsense in\nthe way of whatever type of work you want to do.\n\nMuch of the nonsense left in your head is left there by schools.\nWe're so used to schools that we unconsciously treat going to school\nas identical with learning, but in fact schools have all sorts of\nstrange qualities that warp our ideas about learning and thinking.\n\nFor example, schools induce passivity. Since you were a small child,\nthere was an authority at the front of the class telling all of you\nwhat you had to learn and then measuring whether you did. But neither\nclasses nor tests are intrinsic to learning; they're just artifacts\nof the way schools are usually designed.\n\nThe sooner you overcome this passivity, the better. If you're still\nin school, try thinking of your education as your project, and your\nteachers as working for you rather than vice versa. That may seem\na stretch, but it's not merely some weird thought experiment. It's\nthe truth economically, and in the best case it's the truth\nintellectually as well. The best teachers don't want to be your\nbosses. They'd prefer it if you pushed ahead, using them as a source\nof advice, rather than being pulled by them through the material.\n\nSchools also give you a misleading impression of what work is like.\nIn school they tell you what the problems are, and they're almost\nalways soluble using no more than you've been taught so far. In\nreal life you have to figure out what the problems are, and you\noften don't know if they're soluble at all.\n\nBut perhaps the worst thing schools do to you is train you to win\nby hacking the test. You can't do great work by doing that. You\ncan't trick God. So stop looking for that kind of shortcut. The way\nto beat the system is to focus on problems and solutions that others\nhave overlooked, not to skimp on the work itself.\n\nDon't think of yourself as dependent on some gatekeeper giving you\na \"big break.\" Even if this were true, the best way to get it would\nbe to focus on doing good work rather than chasing influential\npeople.\n\nAnd don't take rejection by committees to heart. The qualities that\nimpress admissions officers and prize committees are quite different\nfrom those required to do great work. The decisions of selection\ncommittees are only meaningful to the extent that they're part of\na feedback loop, and very few are.\n\nPeople new to a field will often copy existing work. There's nothing\ninherently bad about that. There's no better way to learn how\nsomething works than by trying to reproduce it. Nor does\ncopying necessarily make your work unoriginal. Originality is the\npresence of new ideas, not the absence of old ones.\n\nThere's a good way to copy and a bad way. If you're going to copy\nsomething, do it openly instead of furtively, or worse still,\nunconsciously. This is what's meant by the famously misattributed\nphrase \"Great artists steal.\" The really dangerous kind of copying,\nthe kind that gives copying a bad name, is the kind that's done\nwithout realizing it, because you're nothing more than a train\nrunning on tracks laid down by someone else. But at the other\nextreme, copying can be a sign of superiority rather than subordination.\n[25]\n\nIn many fields it's almost inevitable that your early work will be\nin some sense based on other people's. Projects rarely arise in a\nvacuum. They're usually a reaction to previous work. When you're\nfirst starting out, you don't have any previous work; if you're\ngoing to react to something, it has to be someone else's. Once\nyou're established, you can react to your own. But while the former\ngets called derivative and the latter doesn't, structurally the two\ncases are more similar than they seem.\n\nOddly enough, the very novelty of the most novel ideas sometimes\nmakes them seem at first to be more derivative than they are. New\ndiscoveries often have to be conceived initially as variations of\nexisting things, even by their discoverers, because there isn't\nyet the conceptual vocabulary to express them.\n\nThere are definitely some dangers to copying, though. One is that\nyou'll tend to copy old things — things that were in their day at\nthe frontier of knowledge, but no longer are.\n\nAnd when you do copy something, don't copy every feature of it.\nSome will make you ridiculous if you do. Don't copy the manner of\nan eminent 50 year old professor if you're 18, for example, or the\nidiom of a Renaissance poem hundreds of years later.\n\nSome of the features of things you admire are flaws they succeeded\ndespite. Indeed, the features that are easiest to imitate are the\nmost likely to be the flaws.\n\nThis is particularly true for behavior. Some talented people are\njerks, and this sometimes makes it seem to the inexperienced that\nbeing a jerk is part of being talented. It isn't; being talented\nis merely how they get away with it.\n\nOne of the most powerful kinds of copying is to copy something from\none field into another. History is so full of chance discoveries\nof this type that it's probably worth giving chance a hand by\ndeliberately learning about other kinds of work. You can take ideas\nfrom quite distant fields if you let them be metaphors.\n\nNegative examples can be as inspiring as positive ones. In fact you\ncan sometimes learn more from things done badly than from things\ndone well; sometimes it only becomes clear what's needed when it's\nmissing.\n\nIf a lot of the best people in your field are collected in one\nplace, it's usually a good idea to visit for a while. It will\nincrease your ambition, and also, by showing you that these people\nare human, increase your self-confidence.\n[26]\n\nIf you're earnest you'll probably get a warmer welcome than you\nmight expect. Most people who are very good at something are happy\nto talk about it with anyone who's genuinely interested. If they're\nreally good at their work, then they probably have a hobbyist's\ninterest in it, and hobbyists always want to talk about their\nhobbies.\n\nIt may take some effort to find the people who are really good,\nthough. Doing great work has such prestige that in some places,\nparticularly universities, there's a polite fiction that everyone\nis engaged in it. And that is far from true. People within universities\ncan't say so openly, but the quality of the work being done in\ndifferent departments varies immensely. Some departments have people\ndoing great work; others have in the past; others never have.\n\nSeek out the best colleagues. There are a lot of projects that can't\nbe done alone, and even if you're working on one that can be, it's\ngood to have other people to encourage you and to bounce ideas off.\n\nColleagues don't just affect your work, though; they also affect\nyou. So work with people you want to become like, because you will.\n\nQuality is more important than quantity in colleagues. It's better\nto have one or two great ones than a building full of pretty good\nones. In fact it's not merely better, but necessary, judging from\nhistory: the degree to which great work happens in clusters suggests\nthat one's colleagues often make the difference between doing great\nwork and not.\n\nHow do you know when you have sufficiently good colleagues? In my\nexperience, when you do, you know. Which means if you're unsure,\nyou probably don't. But it may be possible to give a more concrete\nanswer than that. Here's an attempt: sufficiently good colleagues\noffer surprising insights. They can see and do things that you\ncan't. So if you have a handful of colleagues good enough to keep\nyou on your toes in this sense, you're probably over the threshold.\n\nMost of us can benefit from collaborating with colleagues, but some\nprojects require people on a larger scale, and starting one of those\nis not for everyone. If you want to run a project like that, you'll\nhave to become a manager, and managing well takes aptitude and\ninterest like any other kind of work. If you don't have them, there\nis no middle path: you must either force yourself to learn management\nas a second language, or avoid such projects.\n[27]\n\nHusband your morale. It's the basis of everything when you're working\non ambitious projects. You have to nurture and protect it like a\nliving organism.\n\nMorale starts with your view of life. You're more likely to do great\nwork if you're an optimist, and more likely to if you think of\nyourself as lucky than if you think of yourself as a victim.\n\nIndeed, work can to some extent protect you from your problems. If\nyou choose work that's pure, its very difficulties will serve as a\nrefuge from the difficulties of everyday life. If this is escapism,\nit's a very productive form of it, and one that has been used by\nsome of the greatest minds in history.\n\nMorale compounds via work: high morale helps you do good work, which\nincreases your morale and helps you do even better work. But this\ncycle also operates in the other direction: if you're not doing\ngood work, that can demoralize you and make it even harder to. Since\nit matters so much for this cycle to be running in the right\ndirection, it can be a good idea to switch to easier work when\nyou're stuck, just so you start to get something done.\n\nOne of the biggest mistakes ambitious people make is to allow\nsetbacks to destroy their morale all at once, like a balloon bursting.\nYou can inoculate yourself against this by explicitly considering\nsetbacks a part of your process. Solving hard problems always\ninvolves some backtracking.\n\nDoing great work is a depth-first search whose root node is the\ndesire to. So \"If at first you don't succeed, try, try again\" isn't\nquite right. It should be: If at first you don't succeed, either\ntry again, or backtrack and then try again.\n\n\"Never give up\" is also not quite right. Obviously there are times\nwhen it's the right choice to eject. A more precise version would\nbe: Never let setbacks panic you into backtracking more than you\nneed to. Corollary: Never abandon the root node.\n\nIt's not necessarily a bad sign if work is a struggle, any more\nthan it's a bad sign to be out of breath while running. It depends\nhow fast you're running. So learn to distinguish good pain from\nbad. Good pain is a sign of effort; bad pain is a sign of damage.\n\nAn audience is a critical component of morale. If you're a scholar,\nyour audience may be your peers; in the arts, it may be an audience\nin the traditional sense. Either way it doesn't need to be big.\nThe value of an audience doesn't grow anything like linearly with\nits size. Which is bad news if you're famous, but good news if\nyou're just starting out, because it means a small but dedicated\naudience can be enough to sustain you. If a handful of people\ngenuinely love what you're doing, that's enough.\n\nTo the extent you can, avoid letting intermediaries come between\nyou and your audience. In some types of work this is inevitable,\nbut it's so liberating to escape it that you might be better off\nswitching to an adjacent type if that will let you go direct.\n[28]\n\nThe people you spend time with will also have a big effect on your\nmorale. You'll find there are some who increase your energy and\nothers who decrease it, and the effect someone has is not always\nwhat you'd expect. Seek out the people who increase your energy and\navoid those who decrease it. Though of course if there's someone\nyou need to take care of, that takes precedence.\n\nDon't marry someone who doesn't understand that you need to work,\nor sees your work as competition for your attention. If you're\nambitious, you need to work; it's almost like a medical condition;\nso someone who won't let you work either doesn't understand you,\nor does and doesn't care.\n\nUltimately morale is physical. You think with your body, so it's\nimportant to take care of it. That means exercising regularly,\neating and sleeping well, and avoiding the more dangerous kinds of\ndrugs. Running and walking are particularly good forms of exercise\nbecause they're good for thinking.\n[29]\n\nPeople who do great work are not necessarily happier than everyone\nelse, but they're happier than they'd be if they didn't. In fact,\nif you're smart and ambitious, it's dangerous not to be productive.\nPeople who are smart and ambitious but don't achieve much tend to\nbecome bitter.\n\nIt's ok to want to impress other people, but choose the right people.\nThe opinion of people you respect is signal. Fame, which is the\nopinion of a much larger group you might or might not respect, just\nadds noise.\n\nThe prestige of a type of work is at best a trailing indicator and\nsometimes completely mistaken. If you do anything well enough,\nyou'll make it prestigious. So the question to ask about a type of\nwork is not how much prestige it has, but how well it could be done.\n\nCompetition can be an effective motivator, but don't let it choose\nthe problem for you; don't let yourself get drawn into chasing\nsomething just because others are. In fact, don't let competitors\nmake you do anything much more specific than work harder.\n\nCuriosity is the best guide. Your curiosity never lies, and it knows\nmore than you do about what's worth paying attention to.\n\nNotice how often that word has come up. If you asked an oracle the\nsecret to doing great work and the oracle replied with a single\nword, my bet would be on \"curiosity.\"\n\nThat doesn't translate directly to advice. It's not enough just to\nbe curious, and you can't command curiosity anyway. But you can\nnurture it and let it drive you.\n\nCuriosity is the key to all four steps in doing great work: it will\nchoose the field for you, get you to the frontier, cause you to\nnotice the gaps in it, and drive you to explore them. The whole\nprocess is a kind of dance with curiosity.\n\nBelieve it or not, I tried to make this essay as short as I could.\nBut its length at least means it acts as a filter. If you made it\nthis far, you must be interested in doing great work. And if so\nyou're already further along than you might realize, because the\nset of people willing to want to is small.\n\nThe factors in doing great work are factors in the literal,\nmathematical sense, and they are: ability, interest, effort, and\nluck. Luck by definition you can't do anything about, so we can\nignore that. And we can assume effort, if you do in fact want to\ndo great work. So the problem boils down to ability and interest.\nCan you find a kind of work where your ability and interest will\ncombine to yield an explosion of new ideas?\n\nHere there are grounds for optimism. There are so many different\nways to do great work, and even more that are still undiscovered.\nOut of all those different types of work, the one you're most suited\nfor is probably a pretty close match. Probably a comically close\nmatch. It's just a question of finding it, and how far into it your\nability and interest can take you. And you can only answer that by\ntrying.\n\nMany more people could try to do great work than do. What holds\nthem back is a combination of modesty and fear. It seems presumptuous\nto try to be Newton or Shakespeare. It also seems hard; surely if\nyou tried something like that, you'd fail. Presumably the calculation\nis rarely explicit. Few people consciously decide not to try to do\ngreat work. But that's what's going on subconsciously; they shy\naway from the question.\n\nSo I'm going to pull a sneaky trick on you. Do you want to do great\nwork, or not? Now you have to decide consciously. Sorry about that.\nI wouldn't have done it to a general audience. But we already know\nyou're interested.\n\nDon't worry about being presumptuous. You don't have to tell anyone.\nAnd if it's too hard and you fail, so what? Lots of people have\nworse problems than that. In fact you'll be lucky if it's the worst\nproblem you have.\n\nYes, you'll have to work hard. But again, lots of people have to\nwork hard. And if you're working on something you find very\ninteresting, which you necessarily will if you're on the right path,\nthe work will probably feel less burdensome than a lot of your\npeers'.\n\nThe discoveries are out there, waiting to be made. Why not by you?\n\nNotes\n\n[1]\nI don't think you could give a precise definition of what\ncounts as great work. Doing great work means doing something important\nso well that you expand people's ideas of what's possible. But\nthere's no threshold for importance. It's a matter of degree, and\noften hard to judge at the time anyway. So I'd rather people focused\non developing their interests rather than worrying about whether\nthey're important or not. Just try to do something amazing, and\nleave it to future generations to say if you succeeded.\n\n[2]\nA lot of standup comedy is based on noticing anomalies in\neveryday life. \"Did you ever notice...?\" New ideas come from doing\nthis about nontrivial things. Which may help explain why people's\nreaction to a new idea is often the first half of laughing: Ha!\n\n[3]\nThat second qualifier is critical. If you're excited about\nsomething most authorities discount, but you can't give a more\nprecise explanation than \"they don't get it,\" then you're starting\nto drift into the territory of cranks.\n\n[4]\nFinding something to work on is not simply a matter of finding\na match between the current version of you and a list of known\nproblems. You'll often have to coevolve with the problem. That's\nwhy it can sometimes be so hard to figure out what to work on. The\nsearch space is huge. It's the cartesian product of all possible\ntypes of work, both known and yet to be discovered, and all possible\nfuture versions of you.\n\nThere's no way you could search this whole space, so you have to\nrely on heuristics to generate promising paths through it and hope\nthe best matches will be clustered. Which they will not always be;\ndifferent types of work have been collected together as much by\naccidents of history as by the intrinsic similarities between them.\n\n[5]\nThere are many reasons curious people are more likely to do\ngreat work, but one of the more subtle is that, by casting a wide\nnet, they're more likely to find the right thing to work on in the\nfirst place.\n\n[6]\nIt can also be dangerous to make things for an audience you\nfeel is less sophisticated than you, if that causes you to talk\ndown to them. You can make a lot of money doing that, if you do it\nin a sufficiently cynical way, but it's not the route to great work.\nNot that anyone using this m.o. would care.\n\n[7]\nThis idea I learned from Hardy's A Mathematician's Apology,\nwhich I recommend to anyone ambitious to do great work, in any\nfield.\n\n[8]\nJust as we overestimate what we can do in a day and underestimate\nwhat we can do over several years, we overestimate the damage done\nby procrastinating for a day and underestimate the damage done by\nprocrastinating for several years.\n\n[9]\nYou can't usually get paid for doing exactly what you want,\nespecially early on. There are two options: get paid for doing work\nclose to what you want and hope to push it closer, or get paid for\ndoing something else entirely and do your own projects on the side.\nBoth can work, but both have drawbacks: in the first approach your\nwork is compromised by default, and in the second you have to fight\nto get time to do it.\n\n[10]\nIf you set your life up right, it will deliver the focus-relax\ncycle automatically. The perfect setup is an office you work in and\nthat you walk to and from.\n\n[11]\nThere may be some very unworldly people who do great work\nwithout consciously trying to. If you want to expand this rule to\ncover that case, it becomes: Don't try to be anything except the\nbest.\n\n[12]\nThis gets more complicated in work like acting, where the\ngoal is to adopt a fake persona. But even here it's possible to be\naffected. Perhaps the rule in such fields should be to avoid\nunintentional affectation.\n\n[13]\nIt's safe to have beliefs that you treat as unquestionable\nif and only if they're also unfalsifiable. For example, it's safe\nto have the principle that everyone should be treated equally under\nthe law, because a sentence with a \"should\" in it isn't really a\nstatement about the world and is therefore hard to disprove. And\nif there's no evidence that could disprove one of your principles,\nthere can't be any facts you'd need to ignore in order to preserve\nit.\n\n[14]\nAffectation is easier to cure than intellectual dishonesty.\nAffectation is often a shortcoming of the young that burns off in\ntime, while intellectual dishonesty is more of a character flaw.\n\n[15]\nObviously you don't have to be working at the exact moment\nyou have the idea, but you'll probably have been working fairly\nrecently.\n\n[16]\nSome say psychoactive drugs have a similar effect. I'm\nskeptical, but also almost totally ignorant of their effects.\n\n[17]\nFor example you might give the nth most important topic\n(m-1)/m^n of your attention, for some m > 1. You couldn't allocate\nyour attention so precisely, of course, but this at least gives an\nidea of a reasonable distribution.\n\n[18]\nThe principles defining a religion have to be mistaken.\nOtherwise anyone might adopt them, and there would be nothing to\ndistinguish the adherents of the religion from everyone else.\n\n[19]\nIt might be a good exercise to try writing down a list of\nquestions you wondered about in your youth. You might find you're\nnow in a position to do something about some of them.\n\n[20]\nThe connection between originality and uncertainty causes a\nstrange phenomenon: because the conventional-minded are more certain\nthan the independent-minded, this tends to give them the upper hand\nin disputes, even though they're generally stupider.\n\n The best lack all conviction, while the worst\n\n Are full of passionate intensity.\n\n[21]\nDerived from Linus Pauling's \"If you want to have good ideas,\nyou must have many ideas.\"\n\n[22]\nAttacking a project as a \"toy\" is similar to attacking a\nstatement as \"inappropriate.\" It means that no more substantial\ncriticism can be made to stick.\n\n[23]\nOne way to tell whether you're wasting time is to ask if\nyou're producing or consuming. Writing computer games is less likely\nto be a waste of time than playing them, and playing games where\nyou create something is less likely to be a waste of time than\nplaying games where you don't.\n\n[24]\nAnother related advantage is that if you haven't said anything\npublicly yet, you won't be biased toward evidence that supports\nyour earlier conclusions. With sufficient integrity you could achieve\neternal youth in this respect, but few manage to. For most people,\nhaving previously published opinions has an effect similar to\nideology, just in quantity 1.\n\n[25]\nIn the early 1630s Daniel Mytens made a painting of Henrietta\nMaria handing a laurel wreath to Charles I. Van Dyck then painted\nhis own version to show how much better he was.\n\n[26]\nI'm being deliberately vague about what a place is. As of\nthis writing, being in the same physical place has advantages that\nare hard to duplicate, but that could change.\n\n[27]\nThis is false when the work the other people have to do is\nvery constrained, as with SETI@home or Bitcoin. It may be possible\nto expand the area in which it's false by defining similarly\nrestricted protocols with more freedom of action in the nodes.\n\n[28]\nCorollary: Building something that enables people to go around\nintermediaries and engage directly with their audience is probably\na good idea.\n\n[29]\nIt may be helpful always to walk or run the same route, because\nthat frees attention for thinking. It feels that way to me, and\nthere is some historical evidence for it.","length":66633,"siteName":"paulgraham.com","publishedTime":null,"image":null},"status":"success","cache_hit":true,"content_quality":{"status":"usable","signals":[],"word_count":11780,"metrics":{"link_density":0.002,"link_count":59,"sentence_ending_ratio":0.063,"repeated_block_ratio":0,"common_word_density":0.269,"list_like_block_ratio":0.721,"structural_block_count":1084}}}