Paul Graham's essay on "How To Do Great Work" begins with the following words:

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

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

The following recipe assumes you're very ambitious.

How To Do Great Work explores curiosity, the source of originality, the relationship between breaking rules and new ideas, and how being naive is a form of independent mindedness. As well as why being self-indulgent helps you find overlooked problems, why big ideas are more often questions than answers, and why the best questions grow while you work to answer them.

A few fascinating bits of background on the essay:

In all, it took nearly 7 months to write. (Source)
It sprung out of a single paragraph in another essay he was writing. It seemed such an important topic that he cut it out and made it into its own essay. (Source)
Reflecting on this last point Paul shared: "It's strange to think that such a huge essay could grow out of one paragraph in another essay. But this has happened before. Beyond Smart began that way too. There's nothing like writing essays to give you ideas for essays." (Source)

It's the best meditation on the conditions and precursors from which Great Work arise. It feels a lot like the modern equivalent to Richard Hamming's talk at Bellcore in 1986 titled You and Your Research.

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The Big Ideas

While nothing beats reading the essay in its entirety, here's an attempt to sum up some of the big ideas:

To do great work, you first have to choose something you a deep interest in and a natural aptitude for — ideally something that offers enough scope to achieve greatness.
Embrace experimentation and always spent some portion of your time on your own projects.
Reach the front of knowledge in your field and notice the gaps in that knowledge. Explore them.
Find value in the cumulative impact of work — be long-term, compounding oriented. Remember that consistency of effort matters more than intensity of effort in the end.
Cultivate taste in your field and strive to be the best.
Be intellectually honest with yourself, admit your mistakes, and stay informal in your approach.
Avoid affectation, cynicism, pessimism, and the need to seem a certain way.
Utilize the advantages of youth (energy, time, optimism, freedom) and the advantage of age (knowledge, efficiency, money, power) at the right time.
Inexperience can be a superpower because it allows you to see things objectively and question established ideas — often because you're entirely unaware of them.
Let your curiosity guide your work. Curiosity is always a precursor to doing great work.
Be prolific and try many things. Just remember to always start small.
People tend to be overly conservative in choosing problems to solve — seek unfashionable and overlooked problems.
Overlooked ideas often hide in plain sight. Explore what's been dismissed, looked over, and left unexplored.
Doing great work means doing something important so well that you expand people's ideas of what's possible.
Just try to do something amazing, and leave it to future generations to say if you succeeded.
A lot of standup comedy is based on noticing anomalies in everyday life. "Did you ever notice...?" New ideas come from doing this about nontrivial things.
Finding something to work on is not simply a matter of finding a match between the current version of you and a list of known problems. You'll often have to coevolve with the problem.
Just as we overestimate what we can do in a day and underestimate what we can do over several years, we overestimate the damage done by procrastinating for a day and underestimate the damage done by procrastinating for several years.
If you set your life up right, it will deliver the focus-relax cycle automatically. The perfect setup is an office you work in and that you walk to and from.
Don't try to be anything except the best.
It might be a good exercise to try writing down a list of questions you wondered about in your youth. You might find you're now in a position to do something about some of them.
"If you want to have good ideas, you must have many ideas." — Linus Pauling
One way to tell whether you're wasting time is to ask if you're producing or consuming. Writing computer games is less likely to be a waste of time than playing them, and playing games where you create something is less likely to be a waste of time than playing games where you don't.

The essay ends with a few reminders and a call to action:

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

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

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

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

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

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

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

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

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How To Do Great Work (Full Essay) by Paul Graham

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

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

The following recipe assumes you're very ambitious.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Don't divide your attention evenly between many topics though, or you'll spread yourself too thin. You want to distribute it according to something more like a power law. [17] Be professionally curious about a few topics and idly curious about many more.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Don't try to cram too much new stuff into any one version. There are names for doing this with the first version (taking too long to ship) and the second (the second system effect), but these are both merely instances of a more general principle.An early version of a new project will sometimes be dismissed as a toy. It's a good sign when people do this. That means it has everything a new idea needs except scale, and that tends to follow. [22]

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

There's a good way to copy and a bad way. If you're going to copy something, do it openly instead of furtively, or worse still, unconsciously. This is what's meant by the famously misattributed phrase "Great artists steal." The really dangerous kind of copying, the kind that gives copying a bad name, is the kind that's done without realizing it, because you're nothing more than a train running on tracks laid down by someone else. But at the other extreme, copying can be a sign of superiority rather than subordination. [25]

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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‍Notes

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

[20] The connection between originality and uncertainty causes a strange phenomenon: because the conventional-minded are more certain than the independent-minded, this tends to give them the upper hand in disputes, even though they're generally stupider.The best lack all conviction, while the worst
Are full of passionate intensity.

[21] Derived from Linus Pauling's "If you want to have good ideas, you must have many ideas."

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

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

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

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

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

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

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

[29] It may be helpful always to walk or run the same route, because that frees attention for thinking. It feels that way to me, and there is some historical evidence for it.

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Originally published on Paul Graham's website.

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Who is Paul Graham?

Most of you will recognize the name. Paul Graham is best known for Y Combinator, which has become the world's foremost startup accelerator whose alumni include Airbnb, Stripe, and DoorDash. In addition, Paul is widely known for his essays including timeless classics, which have become common vernacular, like Default Alive or Default Dead. In 2004, he published a collection of his early essays in a book called Hackers & Painters.

Transcript

Daniel Scrivner (00:02.414)
Paul Graham's essay on how to do great work begins with the following words. If you collected lists of techniques for doing great work in a lot of different fields, what would the intersection look like? I decided to find out by making it. Partly my goal was to create a guide that could be used by someone working in any field, but I also was curious about the shape of the intersection, and one thing this exercise shows is that it does have a definite shape. It's not just a point labeled hard work. The following recipe assumes you're very ambitious.

As we're all both very ambitious and focused on doing great work, it felt appropriate to cover this essay as a sort of book in miniature. The essay itself comes in at a staggering 11,800 words or nearly 30 pages when printed. As such, I think it's appropriate to think of this as more of a monograph than an essay. How to do great work explores curiosity, the source of originality, the relationship between breaking rules and new ideas.

And how being naive is a form of independent mindedness, as well as why being self-indulgent helps you find overlook problems, why big ideas are more often questions than answers, and why the best questions grow while you work to answer them. A few fascinating bits of background on this essay. I did a bit of research because I was curious. In all, it took Paul Graham about seven months to write this. So just to, you know, he said somewhere between six and seven months. In the show notes, I'm going to link to all the sources in case you're curious.

This essay actually sprung out of a paragraph in another essay he was writing. It seemed such an important topic that he cut it out and made it its own separate essay. Reflecting on this last point, Paul shared, it's strange to think that such a huge essay could grow out of one paragraph in another essay, but this has happened before. Beyond Smart, which is one of Paul's other, you know, well-known essays, began that way too. There's nothing like writing essays to give you ideas for other essays. So why am I sharing this?

This post, you know, how to do great work has already been widely read by a lot of different people. Everyone has chimed in, including everyone from Toby Lutke at Shopify, two other founders saying that it's one of the best pieces of writing they've ever read about how to do great work. The reason I wanted to share this is, I mean, one, it's just staggering. Like this is packed with so many amazing, interesting ideas. And we'll get into the structure in a second. And I'll kind of talk about how I understand it and think about what we're covering and why it's important.

Daniel Scrivner (02:21.598)
But the reason I wanted to share this is, you know, we all are very ambitious. We all care about doing great work. This essay is exactly written for us. And so it's something we should study. It's also the best meditation on the conditions and precursors for great work that I've ever read. So I'm going to link to a bunch of stuff in the show notes. I don't imagine this is going to be a short essay because there's so much to explore. And so I'll jump in to a little bit of the essay in just a second.

But if you're curious for my notes, for some of the experts in quotes, for a link to the essay, as well as other related essays like this to me actually feels a lot like a modern equivalent of Richard Hamming's talk that he gave at Bellcore in 1986 titled You and Your Research, You and Your Research, which is another phenomenal piece I'm sure I'll cover at some point in time. Anyways, if you're interested in seeing all of that, I highly encourage you to go find the show notes at outlieracademy.com slash great work.

And you can also, you know, link to the essay. If you haven't read it, you can find it in the show notes for this podcast just directly below. So with that, let's go ahead and jump in. And what I actually want to do is start with where Paul, how Paul ended the essay. So this is all, you know, once you make it 30 pages in, this is what this is what the kind of, you know, last few paragraphs are like at the end. And then we'll jump into the front and start going into the structure of this. Believe it or not, I tried to make this essay as short as I could.

But its length at least means it acts as a sort of filter. If you made it this far, you must be interested in doing great work. And if so, you're already further along than you might realize, because a set of people willing to want to is small. The factors in doing great work are factors in the literal mathematical sense. And they are ability, interest, effort, and luck. Luck by definition, you can't do anything about. So we can ignore that. And we can assume effort if you do in fact want to do great work, it's going to take effort.

So the problem boils down to ability and interest. Can you find a kind of work where your ability and interest will combine to yield an explosion of new ideas? Here there are grounds for optimism. There are so many different ways to do great work and even more that are still undiscovered. Out of all those different types of work, the one you're most suited for is probably a pretty close match. Probably a comically close match. It's just a question of finding it and how far into it your ability and interest can take you. You can only answer that by trying.

Daniel Scrivner (04:42.962)
Many more people could try to do great work than do. What holds them back is a combination of modesty and fear. It seems presumptuous to try to be Newton or Shakespeare. It seems hard. Surely if you tried something like that, you'd fail. Presumably the calculation is rarely explicit. Few people consciously decide not to try to do great work, but that's what's going on subconsciously. They shy away from the question. So it's fascinating here. You know, I'll jump into the essay in a second, but what's fascinating is, you know, as I was kind of preparing for this essay, trying to think about the structure,

It's actually remarkably simple. And I would say, you know, the essay starts out like the, you know, you don't have to be reading for long to get maybe the main jest of Paul's findings of what it takes to do great work. And it's really that he thinks there are four things. The first is that you have to decide what to work on. The second is that you need to learn enough about that so that you can get to the frontier of knowledge in that given field in that given area. The third is that you then, you know, you're on this frontier of knowledge.

You need to notice the gaps. You need to notice where things are missing. You need to notice where little bits of logic or little bits of how this might be done or be done in a better way are missing and can be added. And then the fourth is you need to explore the most promising gaps. And so I would say that's actually relatively simple. What's fascinating is that the bulk of the essay is actually about more of the how. And I kind of think of it as a bunch of tips for navigating and persisting through these seemingly four simple steps.

And it's everything from optimizing for interest in, you know, interestingness, to when ideas are simultaneously novel and obvious, they're usually good ones to why the best questions grow and answering to why everyone should take as much risk as you can afford. So I break all this down in the show notes. And I would say this is probably an episode where I would highly encourage everybody, because there's, you know, everyone should absolutely go and read the essay and that's linked there.

But even just trying to wrap your head around it, it takes quite a while because there's so much ground that Paul covers in the essay. And so, again, highly encourage everyone to go to outlieracademy.com slash great work in order to kind of see how I break this down and be able to see some quotes and excerpts, because I think it's really interesting. OK, so now with that, I'm going to go ahead and dive into the essay. OK, so we're going to start with basically these kind of four rules, these four primers, which I think is really interesting.

Daniel Scrivner (07:06.318)
The first step is to decide what to work on. The work you choose needs to have three qualities. It has to be something you have a natural aptitude for, that you have a deep interest in, and that offers scope to do great work. So all you need to do is find something you have an aptitude for and great interest in. When you're young, you don't know what you're good at and what different kinds of work look like. Some kinds of work you end up doing may not even exist yet. The way to figure out what to work on is by working.

You'll probably guess wrong some of the time and that's fine. One of the things he talks about here that I really like is, and so, you know, just to reiterate, like what is Paul saying in those last few sentences? What he's saying is, you know, you just need to actually start. And I find this somewhat freeing because I think all of us have this natural, you know, we all desire to be, you know, to have like a perfect record where everything that we try out, we are able to be successful at. And I just love, you know, right at the beginning, it's like one, you just need to start.

And you're going to guess wrong some of the time and that's okay. And you know, I think this idea that if you're sufficiently ambitious, you're probably going to want to do more. You're going to have a higher bar for yourself. So that means you're probably going to choose, you know, make some wrong decisions more than people that have a lower bar, you know, lower ambitions. And that's okay. You know, and I think there's something wonderful freeing about that. Wonderfully freeing about that. He also has an idea in here that I really like of just that you want to develop a habit of working on your own projects.

Don't let work mean something other people tell you to do. If you do manage to do great work one day, it'll probably be on a project of your own. Just like a really quick interlude on this, what I find is so fascinating, and the reason I would underscore that advice is, the most talented people I've ever worked with are voracious in their curiosity and their desire to do, and their desire to challenge themselves and try new things.

And you know, this idea of like having your own projects, I think is there's a couple layers to it. On the one hand, it's work on things that you yourself are excited about and give yourself permission to have these kind of side projects or main projects that you're doing. But I think, you know, the other pieces, like it's a core part, everyone needs to have be developing a curriculum for themselves all the time. That's what I'm doing with this podcast. This podcast super selfishly is me.

Daniel Scrivner (09:22.014)
you know, so I'm working to make something incredible for everybody, you know, that is like me, that I think is sufficiently ambitious and interested and curious and wants to get better. But for me, it's a practice. This is a project for myself. So it's a forcing function for me to get really good at this and to get really good at understanding these ideas and articulating them. Okay, enough on that. So just one idea here is you want to develop your own, develop a habit of working on your own projects. What should your projects be?

Whatever seems to you excitingly ambitious as you grow older and your taste in project evolves, exciting and important will converge. But you always want to preserve the excitingness. There's a kind of excited curiosity that's both the engine and the rudder of great work. It'll not only drive you, but if you let it have its way, we'll show you what to work on. What are you excessively curious about? Curious to a degree that would bore most other people.

For me, it's investing. It's a lot of the business books that I cover. That's not an interest that a lot of people share with me, kind of broadly speaking. And so you and I are at a small circle there. You know, but I think that's a great bar. What are you curious and curious to a degree that would bore most other people? What is easy for you that when people see you do it, you know, it looks hard to them. That's what you're looking for. Once you've found something you're excessively interested in, the next step is to learn enough about it to get to one of the frontiers of knowledge.

Knowledge expands fractally, and from a distance, it looks smooth. But once you learn enough to get close to one, they turn out to be full of gaps. So this next piece here, again, you know, going back to kind of the initial framework that we started with here. First, you want to decide what to work on. And you're going to do that by following your curiosity, following what you're most interested in. And, you know, and then you're going to want to get, you know, just get to work.

Second, you're going to want to learn enough about it to get to the frontiers of knowledge. And third, it's about noticing gaps. You know, so the next step is to notice them. Many discoveries have come from asking questions about things that everyone else took for granted. And there's you just an aside for a second. There's some phenomenal footnotes that Paul adds throughout the essay. Some of them are so good. They're interesting enough. I'm going to actually cover them at the end. And so anyways, we just went by one. I'll come back to it at the end.

Daniel Scrivner (11:34.986)
Great work often has a tincture of strangeness. You see this from painting to math. You know, one idea here in terms of how you notice the gaps is to boldly chase outlier ideas, even if other people aren't interested in them. In fact, especially if they aren't. If you're excited about some possibility that everyone else ignores, and you have enough expertise to say precisely what they're overlooking, that's as good a bet as you'll find. I want to read that again, because I think there's a lot of wisdom in the sense.

If you're excited about some possibility that everyone else ignores and you have enough expertise to say precisely what they're all overlooking, that's as good a bet as you'll find. And what I love there is it's kind of like this, this idea or this analogy that you want to be so good. You know, if you're ever going to debate somebody, you want to be able to articulate their point of view so well that you can articulate it better than, than they would be able to themselves. That's how you actually understand the nuance of the subject. And that's how you actually have a, you know, a handle on the idea.

Well, here it feels very similar, you know, and this is a very hard criteria. It's a very high bar. But if you're excited about something that everyone else ignores, and you can say precisely what they're all overlooking, that's as good a bet as any. So again, these four steps, choose a field, learn enough to get to the frontier, notice gaps and explore promising ones. It may not be possible to prove that you have to work hard to do great things. But the empirical evidence is on the scale of the evidence of mortality, which I thought was

That's why it's essential to work on something you're deeply interested in. Interest will drive you to work harder than mere diligence ever will. And you know, we're going to come back to this unsurprisingly one of the keys in this essay, this monograph that we're going to come back to at the end, it's actually echoed at the very end, is that all of this kind of, you know, like great work, if this was a system of planets, great work revolves around curiosity and it revolves around deep passion.

And you know what I love here is it's both the acknowledgement that actually that's something to be followed. You should listen to your intuition and you should listen to just like whatever is, whatever is easy for you. That's not easy for others. Whatever's fascinating for you. That's not typically fascinating for others. Follow those things because one they're energizing. You're going to work harder. You're going to be, you're going to dive deeper.

Daniel Scrivner (13:53.346)
You're going to want to get better at it than other people is just unlocks. So many things, the three most powerful motives, it's going back to the text or curiosity, delight, and the desire to do something impressive. Sometimes they converge. And if you want to create something great, it's exactly what you need. You need these all three motives, curiosity, delight, and desire to create something great. And this, you know, one way I thought about this, I've heard this kind of phenomenal quote recently.

When I hear these powerful motives, but then also the desire to do something impressive, one way I've heard that stated recently, which I really like, is whenever you're looking at anybody, there's a fundamental difference between somebody whose aim is not to lose and someone whose aim is to win. From the outside looking in, they can actually look very similar. They can appear as someone who's working hard, someone who's earnest, but when you really get down to it and the drives and the motivations and the bar, they're very... different.

And so what I love about here again, you know, so you want to, you want to lean into these motives, curiosity, delight, but you especially want to lean into this desire to do something impressive and you want to look for points where they converge because that combination is the most powerful of them all. The big prize is to discover a new fractal bud, you'll notice a crack in the surface of knowledge, pry it open, and there's a whole world inside. And so now you know, we've this is, as I kind of alluded to,

What we've just covered is basically the bulk of the findings. Paul puts it at the very front of the essay. So again, you need to decide what to work on, learn enough about it to get to the frontier of knowledge. You need to notice the gaps in that knowledge. And then we're going to explore, you need to explore, sorry, some of the most promising gaps in that knowledge. The rest of the essay, and so this printed out, I'm on page three, and this is three of 30. So we're 10%, you know.

10% of it is effectively framing up it. The rest of it, I think, are best thought of as a bunch of tips for navigating and persisting through these four simple steps. And so what's fascinating here is it's really not much more complicated than that. But what I love about this essay and really where all of the meat is, is in the remaining 27 pages, where it really is, again, about just tips for making this transition. And what's fascinating structurally...

Daniel Scrivner (16:07.534)
Again, I encourage you to read the essay, but it's actually structured as like there are large gaps between these various ideas. And so you one you can see that this is these are disparate thoughts that are that all cohere together into a narrative. But it's also these kind of many meditations on different ideas, which I really like. OK, let's talk a little bit about the complicated business of figuring out what to work on. So, again, this is all about what to work on.

Which means that the four steps, sorry, the main reason it's hard is that you can't tell what kinds of work are like except by doing them, which means the four steps overlap. You have to work at something for years before you know how much you like it and how good you are at it. The nature of ambition exacerbates the problem. Ambition comes in two forms. I know this was so helpful. One that precedes interest on the subject and one that grows out of it. Most people who do great work have a mix. And the more you have of the former, the harder it will be to decide what to do.

And then he talks about, you know, in the educational systems in most countries, pretend that it's easy. They expect you to commit to a field long before you know what it's really like. And as a result, an ambitious person on an optimal trajectory will often read to the system as an instance of breakage. Be better if they at least admitted it. If they admitted that the system not only can't do much to help you figure out what to work on, but is designed on the assumption that you'll somehow magically guess as a teenager.

Man, is that true? They don't tell you, but I will. When it comes to figuring out what to work on, you're on your own. And then he talks a little bit about this, you know, this kind of concept of, of luck and really gets to the meat of the point, which is that you want to optimize for interestingness. So you need to make yourself a big target for luck. And the way to do that is to be curious, try lots of things, meet lots of people, read lots of books, ask lots of questions. When in doubt, optimize for interestingness.

Fields change as you learn more about them. What mathematicians do, for example, is very different from what you do in a high school math class. So you need to give different types of work a chance to show what they're like, but a field should become increasingly interesting as you learn more about it. Again, this is a great heuristic. So if we're biasing for interest in this, you want to make sure that the deeper you get into something, the more interested you get. And I think just to echo my sense,

Daniel Scrivner (18:26.738)
In my life, the things that have sustained my interest now for a decade or decades have all been things that the deeper I got into them, the more I realized that there was so much more to learn. And it felt like an endless pursuit and endless game in many ways. But it's also something that I, you know, it's your, I think you get excited. It's as if you're progressing at a sport and you continually get more and more excited about your ability to get better and better and better and better. So I would say, you know,

Look for, be aware of that sense, really lean into it. If it doesn't, so if you're not getting more exciting, if you're not getting increasingly interested and energized, then it's probably not for you. If you're making something for people, make sure it's something they actually want. The best way to do this is to make something you yourself want. Write the story you wanna read, build the tool you wanna use. Since your friends probably have similar interests, this will also get you your initial audience. This should follow from the excitingness rule.

Obviously the most exciting story to write will be the one you want to read. The reason I mentioned this case explicitly is that so many people get it wrong. Instead of making what they want, they try to make what some imaginary more sophisticated audience wants. And once you go down that route, you're lost. And just really quickly, I know many people that listen are founders. I think every founder can will resonate with this concept, but there is absolutely like there is deep, profound wisdom in following your own curiosity and in making something that you yourself would love.

And if you can't do that, then you need to be, you need to have an extremely grounded sense of what you're making and who you're making it for. And so I think, you know, this idea of instead of making what they want, they try to make some imaginary more sophisticated audience wants. The reason that that's always a path, you know, you're lost and that's a path of failure is that it's never grounded. You know, typically it's like this amorphous entity.

And you haven't done enough to actually understand deeply what other people want. And so again, you know, if this was an order of hierarchy, it's like first create for yourself. If you can't create for yourself, try to find yourself in what you're creating, but make sure that you're grounding it in this real deep, profound sense of who actually wants this. It can't be this amorphous thing. There are lots of forces that will lead you astray when you're trying to figure out what to work on, pretentiousness, fashion, fear, money, politics, and other people's wishes, imminent frauds. But if you stick to what you find genuinely interesting, you'll be proof against them all.

Daniel Scrivner (20:49.39)
If you're interested, you're not a stray. And this, you know, there's a book that I read a while ago, I've read multiple times now that is, again, it's another set of ideas that rolls around in my head often, and it's by Steven Pressfield, and it's The War of Art. And he, in The War of Art, introduces this concept of resistance, meaning that his whole idea, and this is really deeply rooted in his own

his own work. He's been, Steven Pressfield has been prolific at writing a number of exceptional books, including, you know, so he started out more on the kind of fiction side, you know, writing more narrative and then he moved over to writing self-help and he's now kind of done not self-help, but I guess, you know, books about his craft. And so he talks about the act of creation. He has books on writing. He has books on, one of my favorites is I think it's put your ass where your heart wants to be, which is basically just if you really want to do something you need to put in the work.

But he anyways, in the war of art, he has this idea that has always resonated with me, because it shows up in my life and anyone else's life I've ever seen who wants to accomplish something big, which is that it will never it by nature will not be easy, and there will always be a force that it feels like is working against you. So again, if you're interested, you're not a stray, I think is a really good point there. And know and expect that there's going to be a lot of forces that try to lead you astray, and it's your job to stay focused and to stay to stay grounded.

Okay, moving on a little bit around following your interest. So what I love here was this idea that following your interest is not passive, it's actually active. And so it may sound like a passive strategy, but in practice, it usually means following them past all sorts of obstacles. You usually have to risk rejection and failure, so it does take a good deal of boldness. But while you need boldness, you don't usually need much planning. In most cases, the recipe for doing great work is simply to work hard on excitingly ambitious projects

and something good will come of it. Instead of making a plan and then executing it, you just try to preserve certain invariants. The trouble with planning is that it only works for achievements you can describe in advance. You can win a gold medal or get rich by deciding to as a child and then tenaciously pursue that goal, but you can't discover natural selection that way. I think for most people who want to do great work, the right strategy is not to plan too much. At each stage, do whatever seems most interesting and gives you the best options for the future.

Daniel Scrivner (23:14.238)
I call this approach staying upwind, staying upwind. Love that idea.

Um, one of the other, let's see here. Yeah. What are the other ideas here is, um, again, just how you actually go about persisting. So even when you found something exciting to work on, working on it is not always straightforward. And again, this is like, there's so many tactical ideas in here, but we're about to get to some really good ones. There'll be times when some new ideas make you leap out of bed in the morning and get straight to work, but there will be plenty of times when things aren't like that.

You don't just put out your sail and get blown forward by inspiration. There are headwinds and currents and hidden shoals. So there's a technique to working just as there is to sailing. And you know, the idea that, so this is all kind of a preamble, but what Paul's teeing up is basically this sense of like, you know, one of the core problems, whenever you're working on something difficult is actually working, you know, like getting started on it. And this can be getting started in a given day. You know, I encounter this, everybody encounters this. You have a list of things that you've, you know,

Clearly articulated this what I need to get done today. That does not mean that it's gonna be easy to necessarily jump in and actually start doing it. And Paul describes this as, you know, you need activation energy. It'll probably be harder to start working than to keep working. You'll often have to trick yourself to get over that initial threshold. Don't worry about this, it's the nature of work. It's not a flaw in your character. Work has a sort of activation energy, both per day and per project. And since this threshold is fake in the sense that it's higher than the energy required to keep going,

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

Daniel Scrivner (25:10.866)
I use this trick all the time and it's actually, you know, I, I think of it as like, basically lowering the bar and creating a small, very easy hurdle to go over. And so, you know, some of the ways I apply the same technique is, um, if I'm having challenging, if I'm, if I, you know, I'm aspiring to, uh, read for 30 minutes, I often find it's much more mentally, it's easier for me to get started. It's easier for me to commit to it. It's easier for me to not come up with excuses if I just set a really low bar.

And so what I'll often do is very similar to this idea of just, I'll just read over what I've got so far, which is Paul's, you know, kind of mental trick. My trick is, well, I'll just open up and read for five minutes and I'll put a timer on for five minutes. And the number of times that I will actually only read for five minutes is probably about zero and I will end up reading for 20 or 30 minutes. But anyways, it's a helpful mental trick, helpful way. Again, if you want to accomplish ambitious things, you have to get to work. There's activation energy needed. It's easier to keep going once you've done it.

Don't be afraid of lowering the bar. Make it easy for yourself. Similar techniques work for starting new projects. It's okay to lie to yourself about how much work a project will entail. Lots of great work begins with someone saying, how hard could it be? But what's important is that you try to finish what you start. Even if it turns out to be more work than expected, finishing things is not just an exercise in tidiness or self-discipline. In many projects, a lot of the best work happens in what was meant to be the final stage. This is so true.

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

So Paul then introduces this idea. So we talked about activation energy, you know, so this idea that it takes it, it's a hurdle to get over. It's actually difficult for all of us to get started on something. But once we're started, it's relatively easy. So we talked about that. Now he's going to broaden that out and talk about procrastination and this concept that there's actually multiple different types of procrastination. There's per project procrastination, there's per day procrastination and why per project procrastination is so much worse.

Daniel Scrivner (27:11.338)
Since there are two senses of starting work per day and per project, there are also two forms of procrastination. Per project, procrastination is far more dangerous. You put off starting that ambitious project from year to year because the time isn't quite right. When you're procrastinating in units of years, you can get a lot not done. One reason per project, procrastination is so dangerous is that it usually camouflages itself as work. You're not just sitting around doing nothing. You're working industriously on something else.

Procrastination doesn't set off the alarm bells that per day procrastination does. You're too busy to notice it. And I love this. This is such a like a simple actionable way. The way to beat it is to stop occasionally and ask yourself, Am I working on what I most want to work on? You know, and I often, that's a perfectly wonderful way of you know, asking yourself that question. I think to make that a little bit more meta, maybe a little less prescriptive, I often think of it as like you want to force yourself to reflect.

One of the things that I've learned over time, is that reflection, you know, taking the time to reflect, which is really just saying, you know, like, maybe this bad analogy, but I'll go ahead and use it. You know, imagine we're all various different ships, it's like, most of the time, we're at the captain's wheel, and all we're focused on is what's exactly ahead of us and making sure that we're avoiding obstacles, making sure that we're headed in the right general direction. What we need to force ourselves to do more often is to actually take a bigger step back.

And I think of this as kind of, you know, what are you doing when you do that? Well, you're what you're trying to do is one go higher level. Ray Dalio has talked about this in principles. One of the concepts that he uses is that you want to kind of look down from above. And he talks about this in the concept of work and, you know, you're creating a system and you want to be able to look down on your machine. And he thinks of, you know, what is a machine? Machine could be a business machine, could be the way that you go about investing in some sort of system or process you put together.

But that what you ultimately need to be able to do is like kind of become objective and be able to look out, look down from above and really be able to see things clearly. That is what reflection is all about. You're trying to see reality. You're trying to force yourself to confront some things that you probably are pushing out of your mind. And you're trying to just make sure that you're on the right track. So again, Paul's, you know, kind of approach to this is, am I just stopping occasionally to ask yourself the question? Am I working on what I most want to work on?

Daniel Scrivner (29:36.758)
This next piece I really like, you know, I think a lot of us can conflate time with cost. I know because it's just a very easy connection to make. Like the more time I spend on this, the more it's costing me. The more it's costing me an opportunity cost. You know, what I love about this is just this idea that like great work takes an unreasonable amount of time. It compounds, which requires consistency and just a sense like exponential growth always starts out flat.

And so the way Paul says this is great work usually entails spending what most what would seem to most people an unreasonable amount of time on a problem. You can't think of this time as a cost where it'll seem too high. You have to find the work sufficiently engaging. Again, this goes back to the idea you have to work on stuff that you're not is naturally energizing where you're naturally just very curious. You have to work on, you have to find the work sufficiently engaging as it's happening. There may be some jobs where you have to work diligently for years at things you hate before you get to the good part.

But this is not how great work happens. Great work happens by focusing consistently on something you're genuinely interested in. That's the key, consistency. People who do great work don't get a lot done every day. They get something done rather than nothing done. And what I love about this is, just to connect this for a second, these two sentences are a little bit out of context, but just this idea of like, so great work happens by focusing consistently. Well, why is the consistent piece so important?

Well, it's because compounding, and this is something that I think is hard to internalize, but compounding at the end of the day, or like exponential growth, completely relies on consistency. If you think about something like Warren Buffett's track record, absolutely the core input to that track record is that he has been doing the same thing on the same tact with the same strategy for now nearly 60 years. Wicked consistency over a very long period of time.

And I would say, you know, just one of the things that we all don't want to acknowledge because it's not super sexy is that consistency is a superpower and discipline is a superpower. Um, and it's, you know, but it's difficult and that's okay. But, but if you want to, you know, if you want to do great work, the key is consistency. And so I just love the way he frames it up. You know, people who do great things, they may not get a lot done every day, but they get something done rather than nothing done.

Daniel Scrivner (31:58.798)
And then talks a little bit about like, so consistency, we're doing that for an exponential growth. Well, exponential growth is a little bit different. The trouble with exponential growth is that the curve feels flat in the beginning. It isn't, it's still a wonderful exponential curve, but we can't grasp that intuitively. So we underrate exponential growth. And you know, this is best, like if you're curious for a visual for this look up exponential growth, like just type into Google exponential growth chart.

But I would say you'll see a very different looking chart than a linear chart that goes up and to the right. And this is a concept. I just recorded a book summary for turning the flywheel. It's from Jim Collins. This concept shows up there as well, too. So again, I think just to reroute this, great work takes an unreasonable amount of time. It compounds, which requires consistency.

And exponential growth always feels flat at the beginning. So that's part of why you have to be able to be persistent and be really consistent. If people consciously realize they can invest in exponential growth, many more would do it. This next piece, I kind of think of like a hack. And this is like a short little three paragraph mini essay stuck in the middle of it. But part of this is like when you're doing something great, you also wanna bring your full self to that activity. What do I mean by that?

We all have times where we're obviously sitting down focused on a task. That could be when we're in the office for a given period of time. That could be when we're sitting down at a desk, just focused on one particular task. But I would say greatness, and I think that Paul clearly recognizes this and talks about it, it demands all of you. And you need to make this something that you're always thinking about, that's always on your mind. You're trying to use every ounce of time and energy and effort to be able to get really good at this.

And so just this idea that like work doesn't just happen when you're trying to work. It also happens when you're walking, taking a shower, going to bed, and that, you know, you can think of those times as like undirected thinking times. So you're thinking about something or you could be thinking about something. So why not use that and turn it into directed thinking? Work doesn't just happen when you're trying. There's a kind of undirected thinking you do when walking or taking a shower or lying in bed that can be very powerful. But letting your mind wander a little, you'll often solve problems you were unable to solve by frontal attack.

Daniel Scrivner (34:14.69)
You have to be working hard in the normal way to benefit from this phenomenon though. You can't just walk around daydreaming. The daydreaming has to be interleaved with deliberate work that feeds that feeds it questions. Everyone knows to avoid distractions at work, but it's also important to avoid them in the other half of the cycle. When you let your mind wander it wanders to whatever you care about most at that moment. So avoid the kind of distraction that pushes your work out of the top spot or you'll waste this valuable type of thinking on a distraction instead.

And he says, exception, don't avoid love, which is probably good for us all to remember. He then goes on to talk about just that you want to cultivate your taste. And so, okay, we said, work doesn't just happen when you're trying to work. You want to take your undirected thinking time. You want to make that work. You also want to cultivate taste. Consciously cultivate your taste in the work done in your field until you know which is the best and what makes it so. You don't know what you're aiming for.

And that is what you're aiming for, because if you don't try to be the best, you won't even be good. This observation has been made by so many people in so many different fields that it might be worth thinking about why it's true. It could be because ambition is a phenomenon where almost all the air is in one direction, where almost all the shells that miss the target miss by falling short. Or it could be because ambition...

To be the best is qualitatively different thing from ambition to be good. Again, I just talked about, or you know, is your aim to win or is your aim not to lose? Is your ambition to be the best? You know, and that's a very different thing from just the ambition to be good. Or maybe being good is simply too vague a standard. Probably all three are true.

One way to aim high is to make something that people will care about in 100 years. And I think this is like a really useful principle of, okay, if we're trying to do great work, if we're trying to work on problems that are unbounded, that just have a scope that allows for greatness, then what's maybe a bar we can apply to that? What's one way to be able to gut check that? And I just love this idea because I think it strips whatever your particular goal is of all the bullshit and it focuses you on what's actually important is, you know, like focus ridiculously maniacally on just making something people will care about in a hundred years.

Daniel Scrivner (36:23.926)
That is a very high bar. You know, that is a bar I think that will encourage you to think in a way that is much more durable and in a way that's much more true to who you are. And that's true to really trying to create something that's rooted outside of the noise of what's happening today and is rooted in stuff that's timeless. Just a phenomenal bar.

One of the things he talks about, we're going to talk about this next, is the desire to work in a distinctive style. And you can think about this as, okay, if we're all ambitious, we key in on people that are sources of inspiration for us. This could be people we want to be like. This could be people that we want to emulate. And I think what's wonderful here, and this comes up a little bit more, of just intellectual honesty and leaning into what's true for you and not trying to copycat or be something that you're not.

And I think of that this, you know, my kind of notes on the sidebar was being the best equals you're going to be, you know, you're going to have a distinctive way of working. And so if your goal is to have a distinctive way of working, don't pursue that, just pursue being the best. And if you pursue being the best, that's going to require you to be yourself. That's going to require you to, you know, just set an extraordinarily high bar. And that's going to automatically translate to a distinctive way of working. But it's going to be true to you. So it's not going to be from emulating other people.

Paul says this, Paul says it this way. Don't try to work in a distinctive style, just try to do the best job you can. You won't be able to help doing it in a distinctive way. Style is doing things in a distinctive way without trying. Trying to is affectation. Affectation is in effect to pretend that someone other than you is doing the work. You adopt an impressive fake persona. And while you're pleased with the impressiveness, the fakeness is what shows in the work. So just do the work and your identity will take care of itself.

And he kind of goes off on this, this idea of affectation, which actually had to look up, just understood a little bit better. Avoid affectation is a useful rule so far as it goes. But how would you express this idea positively? How would you say what to be instead of what not to be? The best answer is earnest. If you're earnest, you avoid not just affectation, but a whole set of similar vices. You know, just a profoundly simple thing. Just be earnest. Just literally try to be the best.

Daniel Scrivner (38:44.314)
Set ambitious goals for yourself, like trying to make something that will be relevant, endurable, and useful 100 years from now as it is useful today. And if you do those things, and you approach them just from who you are, you know, then earnestness is exactly what you should do. The core of being earnest is being intellectually honest. We're taught as children to be honest as an unselfish virtue as a kind of sacrifice. But in fact, it's a source of power to see new ideas, you need an exceptionally sharp eye for the truth.

You're trying to see more truth than others have seen so far. Another subtle component of earnestness is informality. Informality is much more important than its grammatical negative name implies. It's not merely the absence of something. It means focusing on what matters instead of what doesn't. What formality and affectation have in common is that as well as doing the work, you're trying to seem a certain way as you're doing it. But any energy that goes into how you seem comes out of being good.

You know, another way of thinking about that's like you're focusing on the veneer. You know, my back, like my backgrounds in design, I've spent a lot of time helping companies, I, you know, achieve their goals of showing up in the world a given way. And, you know, I see a lot of corollaries between this. One of the, a typical conversation with the CEO. So I work with a lot of early stage companies. And every company that I work with has very high ambitions when it comes to their brand, their standards for design, how they want to show up in the world.

Everybody approaches that problem generally in the same way, which is that at first they want to start by copying other people. And I would say that's actually exactly what Paul saying here. You're trying to do affectation. You're trying to say, you know, we're a startup where if you know, say 10 person team with high ambitions, incredibly talented, you know, laser focused on a mission. But you know, what we really want to do is just borrow Apple's design aesthetic or pull from these five companies or these three companies or these two companies.

Well, you know, it's this is a very similar problem that you and I all have, which is we all have a desire to be seen a certain way in the world, or we all have a desire to show up in the world a given way. And what I think is just so useful about this advice, I mean, I've fallen into this trap before, and I think this is a phenomenal reminder, is that, like, you know, this is very hard for founders to be able to grasp, that like, what resonates in a brand is not that something is clean, is not that something looks like an Apple logo, what resonates in a brand is authenticity, in a sense that, you know, a sense of uniqueness.

Daniel Scrivner (41:07.33)
I always, my, you know, the way I kind of describe and think about this today is whenever you're trying to create something, your goal should be to be singular. You want to be the only, you don't want to be one of many, you don't want to be similar, you don't want to be compared to, you want to be one of one. And anyways, and so it's a long way of saying, when I think of avoiding affectation, when I think of being intellectually honest, when I think of informality, you know, and just this idea of like your energy's going into the veneer, it's not going into the substance.

That's what I pull from this and I think it's really helpful. That's one reason nerds have an advantage in doing great work. They expend little effort on seeming anything. In fact, that's basically the definition of a nerd. Be the one who puts things out there rather than the one who sits back and offers sophisticated sounding criticisms of them. The work to great, the route to great work is never easy. The Old Testament says it better to keep quiet lest you look like a fool.

But that's advice for seeming smart. If you actually want to discover new things, it's better to take the risk of telling people your ideas. Some people are naturally earnest, and with others it takes conscious effort. Either kind of earnestness will suffice, but I doubt it would be possible to do great work without being earnest. It's so hard to do even if you are. You don't have enough margin for error to accommodate the distortions introduced by being affected, intellectually dishonest, orthodox, fashionable, we're cool.

So said another way, just strip it all down. You know, I show up authentically, do not try to be anything, just focus on making something great. And if you focus on making something great, and if you lean into your own intuition, and you lean into your own, you know, just the way the thing that you're going to naturally be able to create, it will be distinctive, and it will be distinctive for you, it'd be one of one and be singular and an all I absolutely have a very strong point of view.

That all great work and great work is a very different bar than good work. All great work is singular. And I, you know, anytime I ever feel like I'm struggling to create something, I always try to reroute myself and actually the goals to create something singular. And so what do I need to do at this moment in time to try to do that or push that forward one step more. One of the other things that I like here is just this idea that great work is consistent. And so Paul talks about this. Paul talks about this a little bit.

Daniel Scrivner (43:27.894)
Great work is consistent not only with who did it, but with itself. It's usually all of a piece. So if you face a decision in the middle of working on something, ask which choice is more consistent. You may have to throw things away or redo them. You won't necessarily have to, but you have to be willing to. And that can take some effort. When there's something you need to redo, status quo, bias, and laziness will combine to keep you in denial about it. To beat this ask, if I'd already made the change, would I wanna revert to what I have now?

You know, this idea you have to have the confidence to cut. Don't keep something that doesn't fit just because you're proud of it or because it cost you a lot of effort. Indeed some kinds of work, in some kinds of work, it's good to strip whatever you're doing to its essence. The result will be more concentrated, you'll understand it better, and you won't be able to lie to yourself about whether there's anything real there. Mathematical elegance may sound like a metaphor drawn from the arts. That's what I thought when I first heard the term elegant applied to a proof.

But now I suspect it's conceptually prior, that the main ingredient in artistic elegance is mathematical elegance. You know, maybe another way of saying this is logical elegance. When we see things that cohere together, it's because there's a set of rules, a set of principles that is like the binding element of keeping everything one part. It's a very good sign when it's hard to say whether you're creating something or discovering it.

When you're doing work that could be seen as either creation or discovery, err on the side of discovery. Try thinking of yourself as a mere conduit through which the ideas take their natural self. And then I just love this, you know, sort of simple idea at the end of the section. Great work will often be tool-like in the sense of being something others build on. So it's a good sign if you're creating ideas that others could use or exposing questions that others could answer. The best ideas have implications in many different areas.

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

Daniel Scrivner (45:24.418)
So then we go on to this idea. Let's see here, so great work is consistent. Let's see, okay, just jump into this next section. True by itself is not enough, of course. Great ideas have to be true and new. And it takes a certain amount of ability to see new ideas even once you've learned enough to get to one of the frontiers of knowledge. I've never liked the term creative process. It seems misleading. Originality isn't a process, but a habit of mind.

Original thinkers throw off new ideas about whatever they focus on, like an angle grinder throwing off sparks. They can't help it. I don't know if it's possible to cultivate originality, but there are definite ways to make the most of however much you have. For example, you're much more likely to have original ideas when you're working on something. Original ideas don't come from trying to have original ideas. They come from trying to trying to build or understand something slightly too difficult. And I love this. It's almost like

So what is Paul saying here? This is my interpretation, my notes in the margin, that the originality is a byproduct. It's not a sole aim. And I have found this to be true for many, many different things where what, you know, like the output that you're trying to get is actually a byproduct of doing something and it's not the sole aim. And if you try to treat it as a sole aim, you're going to fail. And so just this idea that if you want to be original.

You're trying, you're basically trying to solve, you're trying to understand something that's beyond your comprehension. And so you're stretching, you're pushing yourself. You're going to have to, you know, there's an aspect of creativity there. There's an aspect of problem solving there. There's an aspect of you're confronted with something that you're a little bit naive about. And, you know, we're going to talk about a little bit of these, some of these topics in a little bit more depth. But I find that very helpful. So again, you know, the fount of origin, the fount of originality is by trying to build or understand something slightly too difficult.

Originality is a byproduct. This is one of the other kind of ideas here. And I love this. Yeah, I love just the metaphor. It also helps. And so again, this is a tip for originality. It also helps to travel and topic space, you'll have more new ideas if you explore lots of different topics, partly because it gives the angle grinder more surface area to work on. And partly because analogies are an especially fruitful source of new ideas. Don't divide your attention evenly between many different topics though or you'll spread yourself too thin.

Daniel Scrivner (47:43.942)
You want to distribute it according to some sort of power law. Be professionally curious about a few topics and idly curious about many more. Curiosity is itself a kind of originality. It's roughly to questions what originality is to answers. And since questions at their best are a big component of answers, curiosity at its best is a creative force. Read this again because I think it's phenomenal. Curiosity is itself a kind of

It's roughly to questions what originality is to answers. So curiosity will, will give you questions to ask. One of the big ideas in here we'll talk about in a little bit is, um, that to find, you know, to do great work, find a great problem in that what you're actually searching for is not a solution. It's not an answer. You're finding a great problem. Um, you know, I've had many, and I can include this in the show notes. Um, one of my, one of the favorite interviews that I've done in the last year was with the founder. Um, it was, it was, uh,

Adrian Allen of the company Forward, who kind of went on a rant when I was interviewing him in the best way possible about why he's so obsessed about being problem focused. And I went into depth, asked him a number of kind of, we went into quite a bit of depth about how this actually materializes what it looks like in the company. But this idea of actually, we're all taught to, we have a natural inclination to be solutions oriented.

And actually what we want at the end of the day to be problem oriented. Because problem, like basically problems, questions is where all the magic is. Okay, so curiosity is itself a kind of answers. Curiosity will give you great questions. And originality is really, you know, it's like originality is a component of a great answer. And so you need a great question first, that's the precursor. And if you're pursuing that question the right way, you know, if you're trying to build or understand something slightly too difficult, if you're being earnest.

If you're leaning into big problems, if you're being okay being naive, if you're showing up as yourself, you're going to get originality out the other side of that equation. I really like this test for, you know, how do you know when you've, how do you spot great ideas? Well, it's typically when they're both true and new. And true by itself is not enough and just that great work is both novel and original.

Daniel Scrivner (49:57.698)
Having new ideas is a strange game because it occasionally consists of seeing things that were right under your nose. Once you've seen a new idea, it tends to seem obvious. Why did no one think of this before? When an idea seems simultaneously novel and obvious, it's probably a good one. And I always think of that like novels actually, you know, so what is novel? Unsurprising novels, a sense of newness, a sense of like, oh, wow, no one's done that before. That's an interesting tweak or twist on it. But what obvious means is that it's actually logical that once you once you

Once someone has proposed this idea to you, it actually snaps right into place and seems like, oh, of course. And so I just love this test. You're looking for ideas that seem simultaneously novel and obvious. We see the world through models that help us, that both help and constrain us. When you fix a broken model, new ideas become obvious. But noticing and fixing a broken model is hard. That's how new ideas can be both obvious and yet hard to discover. They're easy to see after you do something hard.

One way to discover broken models, so again, this is like a source of original and interesting ideas here. One way to discover broken models is to be stricter than other people. Broken models of the world leave a trail of clues where they bash against reality. Most people don't wanna see these clues. It would be an understatement to say that they're attached to their current model. It's what they think in. So they'll tend to ignore the trail of clues left by its breakage, however conspicuous it may seem in retrospect. To find new ideas, you have to seize on signs of breakage instead of looking away.

That's what Einstein did. He was able to see the wild implications of Maxwell's equations, not so much because he was looking for new ideas, as because he was stricter. The idea I wrote myself in The Margin is be stricter. Being stricter, seeing reality more clearly helps you see and discover new ideas and models.

And my interpretation here when I hear models is oftentimes in fields a huge unlock will be proposing a new way that something actually works, a new model of how some, you know, how an input and output happen, a new model of how, you know, cause and effect, a new model of how something works. You know, can you, I think maybe one of the easiest fields to see this in is physics, something like string theory. String theory is a, is a entirely new model by which we would see the world. And so the, you know, what I like here is like, you're both looking, you know, so how are we, are we going to try to do great work? We're going to try to one, be question obsessed.

Daniel Scrivner (52:19.746)
We're going to try to be very earnest in the way that we work on them. You know, we're going to be okay breaking the rules. We're going to talk about that in a second. Just this need to break the rules and why that's a component of, yeah, we think of that as novelness and just really contributing a new note. To contribute a new note, you have to question things and take a different tact and that often requires violating narratives and commonly accepted rules. But just this other idea that you want to be stricter.

You also want to be very, you know, you want to look at the world rigorously. And I think of that as you want to look at the world as really as possible. You want to actually see what's happening as opposed to what sorts of easy, simple, nice, comfortable narratives are kind of sitting on top of it. The other thing you need is a willingness to break rules. If you understand the degree of rule breaking required, because new ideas seem much more conservative once they succeed. They seem perfectly reasonable once you're using the new model of the world brought with them.

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

Okay, so you're looking for narrative, violating ideas, but ideas that aren't bad ideas that actually you know, if you were to kind of carry forward and think about what this actually means if this were true, you start to get really excited and interested in implications instead of just like, oh, well, that's no, there's nothing there. There are two ways to be comfortable breaking rules to enjoy breaking them and to be indifferent to them. I call these two cases being aggressively and passively independent minded. The aggressively independent minded are the naughty ones.

Rules don't merely fail to stop them. Breaking rule gives them breaking rules gives them additional energy for this sort of person delight at the sheer audacity of a project sometimes supplies enough activation energy to get started. The other way to break rules is to not care about them or perhaps not even know they exist. This is why novices and outsiders often make discoveries. Their ignorance of a field's assumptions acts as a source of temporary passive independent mindedness. And so, you know, this is like, I think, pretty deep.

Daniel Scrivner (54:43.99)
But just this idea that, you know, okay, so if you're trying to be original, if you're trying to do great work, you have to have originality. Well, what originality means is that you need to be independent mindedness. And just this concept that there's actually two types of that. You can be aggressively and actively independent minded, and that's probably bad. You know, you don't want to break the rules because you don't know they exist or you're trying to test something, you want to break the rules for the sake of breaking the rules.

And just this idea of, you know, I think of this as like a wonderfully elegant way of explaining why so many new discoveries, why so many new companies are created by people that are new to a field. Well, I think Paul says it here really well, which is the reason that they make these new discoveries is they have an ignorance of a given field's assumptions and that actually acts. And so what is that enabling? Like that, of course they have, you know, of course they have ignorance of assumptions and some common beliefs, but here's the key. It gives them temporary passive, you know, independent mindedness.

So it's helpful. It's helpful in helping them see independently because they're actually coming in not with none of the baggage, none of the frames, none of the rules that are typically being taught. I really like this. This is another thing that Paul, you know, kind of supposes, which is to find good ideas, you actually need to turn off your filters and that a lot of those filters, if you think about the way your mind works, we're always trying to make ourselves feel safe, make ourselves feel comfortable. We're always, you know, we're trying to live in this kind of vacuum and bubble to be super frank.

And so one of the ways of having original ideas is you need to turn some of that off. And I thought this was kind of a wonderful idea. And obviously the idea here is you want to turn off the filters, including some subconscious ones, so that you can get more new ideas. An overlooked idea often doesn't lose till the semi finals. You do see it subconsciously, but then another part of your subconscious shoots it down because it's too weird, too risky, too much work, too controversial.

This suggests an exciting possibility. If you could turn off such filters, you could see more new ideas. One way to do that is to ask what would be, this is phenomenal, it's just phenomenal framing. One way to do that is to ask what would be good ideas for someone else to explore. So simply by making it not about you, make it about the subjective, make believe other person, you know, and what should, what ideas should they go and explore? Then your subconscious won't shoot them down to protect you. You won't be worried about fear of failure. You'll just be anchored on what is interesting.

Daniel Scrivner (57:09.134)
What is something that is sufficiently interesting that it should be explored? And that's where you're anchoring, which I think is really helpful. You could also discover overlooked ideas by working in the other direction, by starting from what's obscuring them. Every cherished but mistaken principle is surrounded by a dead zone of valuable ideas that are unexplored because they contradict it.

Religions are collections of cherished but mistaken principles. So anything that can be described either literally or metaphorically as a religion will have valuable unexplored ideas in its shadow. Copernicus and Darwin both made discoveries of this type. What are people in your field religious about in the sense of being too attached to some principle that might not be as self-evident as they think? What becomes possible if you discard it?

Let's see here. Yeah, one of the other ideas here, which I love, is being problem oriented. And we'll talk a little bit more about that. People show much more originality in solving problems than in deciding what problems to solve. Super interesting insight. Even the smartest can be surprisingly conservative when deciding what to work on. People who'd never dream of being fashionable in any other way get sucked into working on fashionable problems.

One reason people are more conservative when choosing problems and solutions is that problems are bigger bets. I think this is a massive insight. A problem could occupy you for years while exploring a given solution might only take days. But even so, I think most people are too conservative. They're not merely responding to risk, but to fashion as well. Unfashionable problems are undervalued. I've often, you know, I think about this all the time. Of, you know, as a world.

And I think this actually goes back to this idea of avoiding affectation and being earnest. Again, what's the underlying principle there? Well, it's just this idea that we all have a base desire to be fashionable. We want to be seen in a given way. We want to be looked at positively. It's very difficult for us to kind of force ourselves out of that. And I actually think of it as one of the greatest accomplishments that all of us can unlock is this ability to live in discomfort.

Daniel Scrivner (59:16.834)
This ability to live comfortably in fear of failure, this ability to just show up as yourself and not really care about it, because I think it's actually very difficult. And so, how does that translate here? Well, most people are gonna look at for kind of fashionable ideas. One way of saying this would be ideas that they're confident could be achieved in say, shorter timeframe.

Something that feels like the right problem to work on now, as opposed to a problem that I'm not even sure if I can crack it. And if I were, it's going to take me 10 years. You know, that is an unfashionable problem. And just this idea that, you know, you're if you're looking for value, part of that is you're looking for things that are undervalued and that unfashionable problems are undervalued. You know, I think this is articulated in another way. I often think of as just like unsexy problems. It's the same, you know, maybe similar, slightly different wording.

But you know, you want to find the unsexy problems that other people are avoiding, that other people aren't looking at because less you'll have less competition. Of course, that's what you want to do. Great work often takes something that already exists and shows its latent potential. You know, so if you're interested in a field that others think is tapped out, don't let their skepticism deter you. People are often wrong about this.

Working on an unfashionable problem can be very pleasing. There's no hype or hurry. Opportunists and critics are occupied elsewhere. The existing work often has an old school solidity and there's a satisfying sense of economy and cultivating ideas that would otherwise be wasted. But the most common type of overlooked problem is not explicitly unfashionable in the sense of being out of fashion. It just doesn't seem to matter as much as it actually does.

How do you find these? By being self-indulgent, by letting your curiosity have its way in tuning out at least temporarily the little voice in your head that says you should only be working on quote unquote important problems. This is such a key insight and again goes why, you know, if we're trying to do great work, curiosity is at the center because curiosity is maybe another way of saying it's like, it's a very pure force. It is analytical. It is rigorous. It is energized it, um, you know, and uh, yeah.

Daniel Scrivner (01:01:23.722)
And so you always want to be, you don't want to follow your curiosity and let that help you find problems. Because you know, you don't want to just don't look at other signals and don't look to other people. You do need to work on important problems, but almost everyone is too conservative about what counts as one. It's like a challenge for you and I, it is what you're working on too conservative. Are you focused on a solution as opposed to a question? And how could you raise the bar on your ambition?

And I think what I, you know, a big piece that I love about this essay is it is challenging. Like many of the ideas in many ideas in here are uncomfortable because if they're true and you believe in them, then you should be setting a higher bar for yourself. And I think this is a great way of saying that. So try asking yourself if you're going to take a break from quote unquote serious work to work on something just because it would be really interesting. What would you do? The answer is probably more important than it seems.

Daniel Scrivner (01:02:18.372)
Originality in choosing problems seems to matter even more than originality in solving them. So what might seem to be merely the initial step, deciding what to work on is in a sense the key to the whole game.

Few grasp this, and we're going to move on to a slightly different idea here. Few grasp this. One of the biggest misconceptions about new ideas is about the ratio of question to answer in their composition. People think big ideas are answers, but often the real insight was in the question. This is one of my favorite parts of this essay. Part of the reason we underrate questions is the way they're used in schools. In schools, they tend to exist only briefly before being answered like unstable particles. But a really good question can be much more than that. A really good question is a partial discovery.

I love this idea. A really good question is a partial discovery. How do new species arise? Is the force that makes objects fall to earth the same as the one that keeps planets in their orbits? By asking such questions, you are already in excitingly novel territory. By even asking such questions, you are already in excitingly novel territory. What I wrote about this again, just a really good question is a partial discovery and a great question transports you. It's like a little transportation device to new and novel territory.

Get really fucking good at asking questions and coming up with really good questions for yourself. Sometimes you carry a question for a long time. Great work often comes from returning to a question you first noticed years before, even in your childhood, and couldn't stop thinking about. People talk a lot about the importance of keeping your youthful dreams alive, but it's just as important to keep your youthful questions alive. Keep your youthful questions alive.

Think about what's happening at the moment just before a new idea is discovered. Often someone with sufficient expertise is puzzled about something, which means that originality consists partly of puzzlement, of confusion. You have to be comfortable enough with the world being full of puzzles that you're willing to see them, but not so comfortable that you don't want to solve them. It's a great thing to be rich in unanswered questions. I love this, I put a note for myself, strive to be rich in unanswered questions.

Daniel Scrivner (01:04:27.914)
And I feel like just on this for a second, absolutely one of the takeaways for me reading this is I want to spend more time cultivating great questions. I want to be more question obsessed in my own work and in my own pursuit. And I want to anchor more in exciting questions than in exciting answers or exciting solutions. Because I feel like that's just a massive insight. It's a very different way of seeing the world. It's a great thing to be rich in unanswered questions. And this is one of those situations where the rich get richer, because the best way to acquire new questions is to try answering existing questions.

Questions don't just lead to answers, but also to more questions. Again, just to make this connection, I said at the beginning, this essay came out of a paragraph, kind of an unremarkable paragraph from another essay. And so one way of kind of thinking about the genesis of this essay is that this came from a tiny nugget of an idea that was more a question of what does this mean and what would it look like if I dove into this in a big real way. You know, so this work came out of a question. Questions don't just lead to answers, but also to more questions.

And then, you know, it has more ideas about what a great question looks like, which I love. The best questions grow in the answering. You notice a thread protruding from the current paradigm and you try pulling on it and it just gets longer and longer. So don't require a question to be obviously big. So don't require a question to be obviously big before you try answering it. You can actually start with a really small question and it may be that just continuing to pull on that string you get to bigger and bigger and bigger questions. It's like a, you know, it's like a Russian doll of questions.

You can rarely predict that. It's hard enough even to notice a thread, let alone to predict how much will unravel if you pull on it. It's better to be promiscuously curious, to pull a little bit on a lot of threads and see what happens. Big things start small. The initial versions of big things were often just experiments or side projects or talks, which then grew into something bigger. So start lots of small things.

And again, you know, then leading off this idea, you know, one way of interpreting that. And so just this last, you know, my note for this last paragraph was just a note on questions. The best questions grow in answering them. I think that's such a profound, interesting insight. You know, the best questions you get more interested, you get more energized the further into them you get. And this other idea, you want to be promiscuously curious. You want to pull a little bit on a lot of threads. You want to start a lot of small things. Well, what's another way of saying that or looking at that? You want to being prolific is underrated.

Daniel Scrivner (01:06:49.154)
The more different things you try, the greater the chance of discovering new things. Understand, though, that trying lots of things will mean trying lots of things that don't work. You can't have a lot of good ideas without having a lot of bad ones. Though it sounds more responsible to begin by studying everything that's been done before, you'll learn faster and have more fun by just trying stuff. And you'll understand previous work better when you do look at it. So err on the side of starting, which is easier when starting means starting small.

Those two ideas fit together like puzzle pieces. How do you get from starting small to doing something great? By making successive versions, by iterating. Great things are almost always made in successive versions. And one way of thinking about this that I've often thought about is like, why is this true? Why do you wanna start small? And why do all great things that actually cohere? So all big things that actually are impactful and well done, why do they always start small?

Well, you know, I think another way of thinking about this, like you actually have to start, I think about this with teams actually when I'm building teams, like one just insight that I've had is to scale a team to scale a function. So I spend a lot of time in design to scale a design team. You need to have something there to start with. You need to have a core. You need to have, you know, like a seed that's actually gelling. You need to have a gravitational center. And I think the same thing is true when you think about, you know, so ideas that are going to grow and cohere together and be impactful.

I think part of the reason they start small and that you're working in successive iterative versions is you need to start with something of substance that's working. You need to admit one way of thinking about it. Paul earlier in the essay talked about unstable particles. You need your initial small idea needs to be a stable particle. It needs to be something that coheres, something that sparkles, something that you can scale. And then from there, what you're going to do is you're going to just think very iteratively.

And you know, one way I've often thought about that one question I actually ask myself is when working on ideas is just to kind of root myself in this idea that it's iterative and then that I should be less planned and I should be more rooted in just the next right move. One question that I'll ask myself is where should I put the next hour or dollar in a given project? And I feel like what's wonderful about that question is it keeps you rooted in the sense of it's iterative. I don't need to have, I don't need to be thinking necessarily 10 moves ahead.

Daniel Scrivner (01:09:13.378)
If I just, you know, have something of quality that I'm working on. It can be very, very small. But if I'm working to grow bigger, I just need to make the next right move and the next right move. And I feel like that mode is uncomfortable, but that's also what gets us to compounding this idea of just being consistent, working, starting small, doing successive versions. It all coheres together. You start with something small and evolve it. And the final version is both clever and more ambitious than anything you could have planned.

It's particularly useful to make successive versions when you're making something for people to get an initial version in front of them quickly and then evolve it based on their response. Begin by trying the simplest thing that could possibly work. Surprisingly often, it does. If it doesn't, this will at least get you started. If you keep projects small and use flexible media, you don't have to plan as much and your designs can evolve instead. You know, one way of thinking about that is like you're working on an idea or a project, you're working on it emergently. You're starting with something.

And this act of being iterative, I think honestly, what that allows is for something to emerge slowly over time. Like one of the other ideas that I have along these lines of allowing something to emerge is in creative process. You know, if we're working on, say, a new product design, one of the things that you want to do, like one of the big topic conversations I have with founders often is around how to set design teams up for success.

And a counterintuitive insight is that what a successful project, what a successful process looks like for a design team or a product team is that they allow themselves to surprise themselves to come up with surprising answers. And that may not sound very profound, but there's a bunch of precursors that are very obvious. If you want to be able to surprise yourself, one, you can't start with a crystal clear idea of what you want to be able to build. Sure, you absolutely want to start with some idea, you know, some like frame of reference or some sense sense of the ambition.

But what you actually want to do is more focus on questions and not answers. And you want to bake in enough time upfront to really be able to look at multiple different ideas and triangulate and to allow something to emerge. And so again, just this idea of like great work is often emergent. You want to get to something great and big and ambitious, it always starts small. And it's great to work iteratively. Great things are almost always made in successive versions.

Daniel Scrivner (01:11:35.07)
Okay, now switching to this topic of risk, you know, just a very straightforward insight. You want to take as much risk as you can afford. Every project that fails can be valuable in the process of working on it. You'll have cross territory. Few others have seen and encountered questions. Few others have asked, and there's probably no better source of questions than the ones you encounter in trying to do something slightly too hard. This, I mean, this is like just a profound, interesting insight.

Use the advantages of youth when you have them and the advantages of age once you have those. The advantages of youth are energy, time, optimism, and freedom. The advantages of age are knowledge, efficiency, money, and power. With effort, you can acquire some of the latter when young and keep some of the former when old. The old also have the advantage of knowing which advantages they have. The young often have them without realizing it. The biggest is probably time. The young have no idea how rich they are in time.

The best way to turn this time to advantage is to use it on slightly frivolous ways to learn about something you don't need to know about just out of curiosity or by trying to build something just because it would be cool or become freakishly good at something that slightly is an important qualification. Spend time lavishly when you're young, but don't waste it. There's a big difference between doing something you worry might be a waste of time and doing something you know for sure will be. The former is at least a bet and possibly a better one than you think.

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

One of the most valuable kinds of knowledge you get from experience is to know what you don't have to worry about. The young know all the things that could matter, but not the relative importance. So they worry equally about everything. When you should worry more about a few things and hardly at all about the rest. But what you don't know is only half the problem with an experience. The other half is what you know that ain't so. You arrive at adulthood with a head full of nonsense, bad habits you've acquired and false things you've been taught.

Daniel Scrivner (01:13:53.886)
and you won't be able to do great work till you clear away at least the nonsense in the way of whatever type of work you want to do. For example, schools induce passivity. Since you were a small child, there was an authority at the front of the class telling you what to do, telling you what you had to learn, and then measuring whether you did it. But neither classes nor tests are intrinsic to learning. They're just artifacts of the way schools are usually designed. The sooner you overcome the passivity, the better.

The best teachers don't wanna be bosses. They'd prefer it if you pushed ahead using them as a source of advice rather than being pulled by them through the material. Schools also give you a misleading impression of what work is like. The way to beat the system is to focus on problems and solutions that others have overlooked, not to skimp on the work itself.

Daniel Scrivner (01:14:42.966)
This I really like so we can talk a little bit about originality but also about good and bad ways to copy and I think there's actually some profound ideas in here. People new to a field will often copy existing work. There's nothing inherently bad about that. There's no better way to learn how something works than by trying to reproduce it. Nor does copying necessarily make your work unoriginal. Love this next sentence. I'm gonna say it twice. Originality is the presence of new ideas not the absence of old ones. Originality is the presence of new ideas not the absence of old ones.

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

In many fields, it's almost inevitable that your early work will be in some sense based on other people's projects rarely arise in a vacuum. Once you're established, you can react to your own. But while the former gets called derivative, the latter doesn't structurally, the two cases are more similar than they seem. So again, just like this idea of and this is just so true in life, like whenever you're learning something new. I think copying is actually wonderful, you know, and

What do I mean by that and why is it a positive thing? Well, I think part of copying is trying to figure out your tone and your voice and your take. And again, I have a profound belief, Paul echoes it in here, that what's the best way to learn about something? I think of it as like, you need to come into reality, you need to come into contact with it, because your only way you get to ground truth is by actually trying and doing. You have to get out of hypothesis and theses and what do I think could happen, and you just need to jump in and start doing it. And I would say,

You know, one of the ideas in this essay is like, just start, find something, be okay making some mistakes, be okay taking some risks, be okay intellectually honest with yourself about what's working and what's not, but try something. And you know, be unafraid to copy. But what you want to do is you want to, you know, just like remember that you can copy in the sense of using old ideas, ideas that aren't yours, ideas that have been in the industry or in the vein of work for a long period of time.

Daniel Scrivner (01:17:01.846)
But ultimately, great work has originality, it has some novelty to it. And so, originality is a presence of new ideas. And so ideally, don't copy outright, don't copy wholesale, but copy and then modify. And I would say one of the best ways, one of the best ways I would say to copy well is to copy from many different places and be a master at conglomerating those things together. Because often new ideas are the amalgamation of a bunch of surprising other ideas that no one's tried fitting together.

Some of the features of things you admire are flaws they succeeded despite of. Indeed, the features that are easiest to imitate are the are most likely to be the flaws. This is particularly true for behavior. Some talented people are jerks, and this sometimes makes it seem to the experience that being a jerk is part of being talented. It isn't. Being talented is merely how they got that way. One of the most powerful kinds of copying is copying something from one field into another.

Daniel Scrivner (01:18:02.23)
That it's probably worth giving chance a hand by deliberately learning about other kinds of work. You can take ideas from quite distant fields if you let them be metaphors. Metaphors like this wonderful abstraction layer. I can take an idea from one field, I can try to abstract it slightly by turning it into a metaphor, and I can take that almost like a piece of a game or a Lego block and go and apply it somewhere else. Negative examples can also be as inspiring as positive ones.

In fact, you can sometimes learn more from things done badly than from things done well. Sometimes it only becomes clear what's needed when it's missing. If a lot in this then very different tangent. So that was the end of that idea of just you know kind of copying what that means, good ways to copy, bad ways to copy, and that oftentimes when you try to copy outright you're actually copying the flaws. You're copying, one way I've thought about it is you're copying the output and not the input that got that output.

Daniel Scrivner (01:19:00.506)
Yeah, I won't share a reference there. There's plenty that come to mind, but I feel like that captures the idea well. Okay, so this is very different. This is almost like a call to action of a way, again, if you want to do great work, we're now going to talk about the people aspect of that. If a lot of the best people in your field are collected in one place, it's usually a good idea to visit for a while.

It will increase your ambition and also by showing you that these people are human, increase your self-confidence. If you're earnest, you'll get a warmer welcome than you might expect. Most people who are very good at something are happy to talk about it with anyone who's genuinely interested. If they're really good at their work, then they probably have a hobbyist interest in it and the hobbyist always want to talk their hobbies.

Daniel Scrivner (01:19:47.674)
So related to this, so that idea, one way of saying it's like, if you want to be the best in the world at something, go and find out where many of the most talented people are and you want to go put yourself in that network. This is why if you're a founder, historically the advice would be to go to Silicon Valley. It's still great advice, although now there are multiple hubs where there are amazing founders and amazing investors and incredible talent employees that want to work in early stage companies. But it's an easy hack. And I just love the note because I think it's very true.

Part of going there and being there in person is just you actually come and counter with other people that are doing this at a really high level. And you will, in my case, maybe I'll frame it that way, it's probably more accurate. In my case, I've had the chance to work with exceptionally talented people. Keith Raboy at Square, who's now gone on to Open Door, Founders Fund, Jack Dorsey, profoundly talented executives that have gone on to do some really amazing things.

And you absolutely find by working with those people, I would say it's kind of a 50-50 case of things that are intimidating about how good they are and aspects of what they do. And from that, you can pull so much inspiration and you can pull so many ideas of how you can tactically get better or strategically get better. But similarly, you're gonna find out that they're human and you're gonna find out that, you know, everybody has rough edges and corners and things that they have to work on and things that they're not great at. And part of becoming successful is learning how to work around those things.

And you know, just disabuse yourself of this notion that anybody does not have things, you know, that cannot be improved. And you know, why is this all important? Well, sure, we're all imperfect. But I think, you know, Paul captures the right idea that a big part of just doing great work is having the confidence that you can. And part of that confidence, I would say, is, you know, knowing, knowing people that have done great work and knowing that they're humans, knowing that, you know, they're not all that different. Okay.

Similar but different idea, you know, so you want to obviously want to seek out the best colleagues. You know, there are a lot of projects that can't be done alone. And even if you're working on one that can be, it's good to have other people encourage you and to bounce ideas off of absolutely. Colleagues don't just affect your work, though. They also affect you. So work with people you want to become like because you will work with people you want to become like. So you will quality is more important than quantity and colleagues. It's better to have one or two great ones than a building full of pretty good ones. Amen.

Daniel Scrivner (01:22:09.666)
In fact, it's not merely better, but necessary judging from history. The degree to which great work happens in clusters suggests that one's colleagues often make the difference between doing great work and not. How do you know when you have sufficiently good colleagues? In my experience, when you do, you know. Which means if you're unsure, you probably don't. But it may be possible to give a more concrete answer than that. Here's an attempt. Sufficiently good colleagues offer surprising insights. They see and do things that you can't.

So if you have a handful of colleagues good enough to keep you on your toes in the sense you're probably over the threshold. And I think that's exactly right. What is the bar for good colleagues? Good colleagues are, there's a degree to it that it's intimidating. It makes you wanna show up with your A game. It makes you want to contribute at the level that they're contributing. And it makes you want to combine your efforts to really create something that either of you independently would not be able to create.

Most of us can benefit from collaborating with colleagues, but some projects require people on a larger scale. And starting one of those is not for everyone. If you want to run a project like that, you'll have to become a manager. And managing well takes aptitude and interest like any other kind of work. If you don't have them, there is no middle path. You must either force yourself to learn management as a second language or avoid such projects. This next piece I love, which is obviously if you're going to work on something ambitious, morale is critically important.

And so the kind of meta note here is like husband your morale. It's the basis of everything when you're working on ambitious projects. You have to nurture and protect it like a living organism. Morale starts with your view of life. You're more likely to do great work if you're an optimist and more likely if you think of yourself as lucky than if you think of yourself as a victim. Morale also compounds by a work. High morale helps you do good work, which increases your morale and helps you do even better work. Maybe said another way.

morale works like a flywheel. You want to have a positive flywheel of morale. One of the biggest mistakes ambitious people make is to allow setbacks to destroy their morale all at once, like a balloon bursting. You can inculcate yourself against this by explicitly considering setbacks as part of the process. Again, explicitly considering setbacks as part of the process. Solving hard problems involves some backtracking. I'm gonna stop here for a second just to add a meta-reflection.

Daniel Scrivner (01:24:28.522)
I used to have a belief that you know, that optimism meant that I should expect that there are no setbacks and I should expect that, you know, I should just have an unrealistic view about how things would go. And I would say as I've done more ambitious things, as I've gotten older, as I've had success and failure, I feel like that's been tempered and it's accurately reflected in how Paul Graham talks about it here, which is now I think about optimism as I have an undeniable underlying belief that I can overcome.

And then I can figure something out and then I can persist. But I have no, I know that it won't be easy. I know that there'll be setbacks and I know there'll be surprises. I know that there'll be periods where I feel wrong and stuck and like I can't make progress. And I would say that version of optimism that's tempered with reality is so much more helpful than a version of optimism that is tempered in just an unrealistic view of the world. And so I love here.

It's like you want to be optimistic, you want to work with ambitious people, but you also want to, you know, understand that there's going to be setbacks. You want to see that as part of the process. Why? Because then you're not going to be surprised if you know so much of reality and our emotional realities based off our expectations. I just think that's profound. So if at first you don't succeed, try, try again isn't quite right. It should be if at first you don't succeed either try again or backtrack and then try again.

Never give up is also not quite right. Obviously there are times when it's the right choice to eject. Or more precise version would be, never let setbacks panic you into backtracking more than need be. Corollary, never abandon the root node. It's not necessarily a bad sign if work is a struggle, any more than it's a bad sign to be out of breath while running. Such a good insight. It depends how fast you're running. So learn to distinguish good pain from bad. Good pain is a sign of effort. Bad pain is a sign of damage.

Daniel Scrivner (01:26:22.026)
One of the things that Paul talks about here, which is, you know, I think is helpful to reiterate is, you know, there's a physical component of doing great work. And I think that's not talked about enough. Like one of the insights I've had, and we'll get into how this relates to Paul's thoughts in a second, but one of the insights I've had is, you know, if you look at successful people, by and large, they tend to be much more athletic and focused on physical health and just, you know, being at the top of their physical capabilities than people that aren't.

And I would say one way of thinking about that is actually just to record. It's not that these people are superhuman. It's not that these people really care, you know, about looking and feeling good. But it's not, it's important. And I think they see, they see the, they know that they're how they're feeling physically and their physical body. It will color everything else that they do. And so again, it's just the idea of like, if you have, if you want to do great work, if you want to have a very high bar for yourself, if you want to be able to persist over decades, you need to care for yourself physically. You're one.

whole entity. And so I just love, you know, a couple of lines from this essay that relate to that. Ultimately, morale is physical. You think with your body, so it's important to take care of it. That means exercising regularly, eating and sleeping well, and avoiding the most dangerous kinds of drugs. Running and walking are particularly good forms of exercise because they're good for thinking. People who do great work are not necessarily happier than everyone else, but they're happier than they'd be if they didn't.

In fact, if you're smart and ambitious, it's dangerous not to be productive. People who are smart and ambitious but don't achieve much tend to become bitter. It's okay to want to impress other people but choose the right people. The opinion of people you respect is signal. Fame, which is the opinion of a much larger group you might or might not respect, just adds noise. The prestige of a type of work is at best a trailing indicator and sometimes completely mistaken. If you do anything well enough, you'll make it prestigious.

Competition can be an effective motivator, but don't let it choose the problem for you. Don't let yourself get drawn into chasing something just because others are. In fact, don't let competitors make you do anything much more specific than work harder. Again, curiosity is the best guide. Your curiosity never lies and it knows more about you, more than you do about what's worth paying attention to. Notice how often the word has come up.

Daniel Scrivner (01:28:42.75)
If you asked an oracle the secret, and I think this is all profound and we'll start wrapping up here in a second. We're almost at the end of the essay. And so this, you know, is the conclusion of just rerouting it in curiosity. If you asked an oracle the secret to doing great work and the oracle replied with a single word, my bet would be on curiosity. It doesn't translate directly to advice. It's not enough just to be curious. You can't command curiosity anyway, but you can nurture it and you can let it drive you. Curiosity is the key to all four steps in doing great work.

It'll choose the field for you, get you to the frontier, cause you to notice gaps in it, and drive you to explore them. The whole process is a kind of curiosity. So again, I'll just read the last bit of this because I think it's too good not to read again. And so this is how Paul closes the essay. I'm then gonna end with a couple of footnotes because those are really great, but we're nearly there. Okay, so here's the closing.

Believe it or not, and you know now, we've been talking about this, we've been going through this essay for 90 minutes. So there's, and hopefully I have done a good job of exposing the wealth of insights that I found inside this. Because my whole job, my whole goal with these is to not only use this as a way for me to really meditate on this, be able to articulate these thoughts, but I want to be an amazing conduit for compressing and distilling these for other people. Believe it or not, I tried to make this essay as short as I could.

But its length at least means it acts as a filter. If you made it this far, you must be interested in doing great work. And if so, you're already further along than you might realize, because the set of people willing to want to is small. The factors in doing great work are factors in the literal mathematical sense, and they are ability, interest, effort, and luck. Luck by definition, you can't do anything about, so we can ignore that. And we can assume effort if you do in fact wanna do great work. So the problem boils down to ability and interest.

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

Daniel Scrivner (01:31:05.394)
Many more people could try to do great work than do. What holds them back is a combination of modesty and fear. It seems presumptuous to try to be Newton or Shakespeare. It also seems hard. Surely if you tried something like that, you'd fail. Presumably the calculation is rarely explicit. Few people can consciously decide not to try to do great work, but that's what's going on subconsciously. They shy away from the question. So I'm gonna pull a sneaky trick on you. Do you wanna do great work or not? Now you have to decide consciously. Sorry about that.

I wouldn't have done it to a general audience, but we already know you're interested. Don't worry about being presumptuous, you don't have to tell anyone. And if it's too hard and you fail, so what? Lots of people have worse problems than that. In fact, you'll be lucky if it's the worst problem you have. Yes, you'll have to work hard, but again, lots of people have to work hard. And if you're working on something you find very interesting, which you necessarily will if you're on the right path, the work will probably feel less burdensome than a lot of your peers.

Discoveries are out there waiting to be made. Why not by you?" So that was, I'll end in a second by just tossing in a couple of the footnotes that I really enjoyed. But that was How to Do Great Work. It's an incredible essay, 11,800 words. Took me 90 minutes to go through and talk through. And you can find more about it.

You can see all of my notes, excerpts, quotes, some amazing stuff at outlieracademy.com/great-work. And I'm gonna end with just a couple of footnotes. And so one of the things I really like, I rarely do this, I always notice when people will add basically notes or footnotes to a document. And as I was reading this, I started noting like, wow, there's actually kind of a lot. I think in total there's 20, something like that, 20, 29, 29 footnotes. And some of them are just great. So I thought I couldn't conclude without including some of those.

So I'm just going to talk through them really quickly. These are some of my favorites. Doing great work means doing something important so well that you expand people's idea of what's possible. You know, my takeaway from that is that that's actually the definition of great work. One of the things I really like collecting is, you know, definitions of words or terms that feel personal to me and have significance.

Daniel Scrivner (01:33:23.07)
Just try to do something amazing and leave it to future generations to say if you exceeded. I think it's a great way of kind of taking the pressure off of yourself. Again, aim to create something that's as relevant 100 years from now. Just aim to create something amazing and don't worry about judgment. Don't worry about judgment now. I thought this insight was interesting. A lot of stand-up comedy is based on noticing anomalies in everyday life. Did you ever notice? Dot, dot, dot.

New ideas come from discovering this about non-trivial things. It's about noticing anomalies. Finding something to work on is not simply a matter of finding a match between the current version of you and a list of known problems. You'll often have to co-evolve with the problem. This was an interesting way of thinking about how you might pursue a problem, how you might spar with the problem through time. You know, you might, you know, you'll often have to co-evolve with the problem.

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

If you set your life up right, it will deliver the focus, relax cycle automatically. The perfect setup is an office you work in, in that you walk to and from. So obviously, you know, one of the things we talked about a lot here is just doing great work is all encompassing. It requires all of you. Um, and just this idea that of course, a piece of that, because doing great work is going to mean you're going to have to pursue a big problem that allows for greatness over a long period of time. You're going to need to move between focus and relaxation and just this idea that, you know, keep that front of mind.

Think about how you can set that up in your life so you can enable yourself to be able to really persist over the longest period of time possible. That's how compounding works. Consistency over long periods of time. Don't try to be anything except the best. I think that's a great, ridiculously simple takeaway to take away from this. Just focus on being the best. Be earnest. It'd be a good exercise to try writing down a list of questions you rendered about in your youth. Again, this idea of like keeping your youthful questions alive.

Daniel Scrivner (01:35:25.994)
You might find you're now in a position to do something about them. I haven't done this exercise. I don't know if I'd have anything particularly insightful, but someone listening might. So I encourage you all to think about that. Are there questions from your youth you might want to rethink about?

You talk to this idea, you know, I think it's just helpful to keep in mind. If you want to have good ideas, you must have many ideas. Another way of saying that's if you want to have good ideas, you must have bad ideas. Bad ideas are a precursor to good ideas. It's absolutely essential. Bad works, you know, is a precursor to great work. A shitty draft of an essay is a precursor to a great draft of an essay. Start small, work on something that's stable that has substance, work iteratively.

One way to tell whether you're wasting time is to ask if you're producing or consuming. This was a really interesting question. Writing computer games is less likely to be a waste of time than playing them. And playing games where you create something is less likely to be a waste of time than playing games where you don't. So one way to tell if you're wasting time is to ask whether you're producing or consuming. OK, I will leave it there. Again, I highly encourage you to read How to Do Great Work in full.

You can find a link to that essay in the show notes below this podcast, this video on YouTube. You can find my notes as well as my favorite excerpts and quotes from this essay at outlieracademy.com slash great work. You can also subscribe to the podcast there. You can find all of our previous episodes. We've got 160 plus now. And then finally to get my top 10 highlights from this essay. So I, everything that, everything that I go through and share here, I ultimately distill down, it's a great forcing function for me into my top 10 highlights.

It's a great way for me to say just, you know, in this case I read 11,800 words. What are the 10 highlights that I want to save that for me, I will think of as if I reread those that's kind of getting the essence, the distillation of this idea. I do this for everything and I share this. And so if you're interested in getting this, I do it for every book, letter speech that I share, sign up for my email list at newsletter.outlieracademy.com. That's newsletter.outlieracademy.com. Thank you so much. And again, this was a summary, really more of like a deep dive dissection of How to Do Great Work by Paul Graham.

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#168 Essay Breakdown: “How To Do Great Work” by Paul Graham

#168 Essay Breakdown: “How To Do Great Work” by Paul Graham

The Big Ideas

How To Do Great Work (Full Essay) by Paul Graham

Who is Paul Graham?

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#168 Essay Breakdown: “How To Do Great Work” by Paul Graham

#168 Essay Breakdown: “How To Do Great Work” by Paul Graham

The Big Ideas

How To Do Great Work (Full Essay) by Paul Graham

Who is Paul Graham?

Transcript

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