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.
[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.
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.
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.
[7]
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]
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.
[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.)
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.
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.
"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]
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.
[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.
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.
[18]
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.
[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.
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.
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.
[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.
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.
[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.
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.
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]
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.
[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.
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?
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.
Thanks
to Trevor Blackwell, Daniel Gackle, Pam Graham, Tom Howard,
Patrick Hsu, Steve Huffman, Jessica Livingston, Henry Lloyd-Baker,
Bob Metcalfe, Ben Miller, Robert Morris, Michael Nielsen, Courtenay
Pipkin, Joris Poort, Mieke Roos, Rajat Suri, Harj Taggar, Garry
Tan, and my younger son for suggestions and for reading drafts.