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July 2023  
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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.   
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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.   
  
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.  
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
  
  
  
  
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.   
  
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.   
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.)  
  
  
  
  
  
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.   
  
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.  
  
  
  
  
  
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.   
  
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.  
  
  
  
  
  
"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.   
  
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.   
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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.  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.  
  
  
  
  
  
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.  
  
  
  
  
  
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.  
  
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?  
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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.  
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.
  
  
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.  
  
  
  
  
  
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.  
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.  
  
  
  
  
  
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 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.  
  
  
  
  
  
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.
  
  
  
  
  
  
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.  
  
  
  
  
  
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.   
  
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.   
  
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 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.  
  
  
  
  
  
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.  
  
  
  
  
  
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?  
  
  
  
  
  
  
  
  
  
**