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November 2019  
  
Everyone knows that to do great work you need both natural ability and
determination. But there's a third ingredient that's not as well understood:
an obsessive interest in a particular topic.  
  
To explain this point I need to burn my reputation with some group of people,
and I'm going to choose bus ticket collectors. There are people who collect
old bus tickets. Like many collectors, they have an obsessive interest in the
minutiae of what they collect. They can keep track of distinctions between
different types of bus tickets that would be hard for the rest of us to
remember. Because we don't care enough. What's the point of spending so much
time thinking about old bus tickets?  
  
Which leads us to the second feature of this kind of obsession: there is no
point. A bus ticket collector's love is disinterested. They're not doing it to
impress us or to make themselves rich, but for its own sake.  
  
When you look at the lives of people who've done great work, you see a
consistent pattern. They often begin with a bus ticket collector's obsessive
interest in something that would have seemed pointless to most of their
contemporaries. One of the most striking features of Darwin's book about his
voyage on the Beagle is the sheer depth of his interest in natural history.
His curiosity seems infinite. Ditto for Ramanujan, sitting by the hour working
out on his slate what happens to series.  
  
It's a mistake to think they were "laying the groundwork" for the discoveries
they made later. There's too much intention in that metaphor. Like bus ticket
collectors, they were doing it because they liked it.  
  
But there is a difference between Ramanujan and a bus ticket collector. Series
matter, and bus tickets don't.  
  
If I had to put the recipe for genius into one sentence, that might be it: to
have a disinterested obsession with something that matters.  
  
Aren't I forgetting about the other two ingredients? Less than you might
think. An obsessive interest in a topic is both a proxy for ability and a
substitute for determination. Unless you have sufficient mathematical
aptitude, you won't find series interesting. And when you're obsessively
interested in something, you don't need as much determination: you don't need
to push yourself as hard when curiosity is pulling you.  
  
An obsessive interest will even bring you luck, to the extent anything can.
Chance, as Pasteur said, favors the prepared mind, and if there's one thing an
obsessed mind is, it's prepared.  
  
The disinterestedness of this kind of obsession is its most important feature.
Not just because it's a filter for earnestness, but because it helps you
discover new ideas.  
  
The paths that lead to new ideas tend to look unpromising. If they looked
promising, other people would already have explored them. How do the people
who do great work discover these paths that others overlook? The popular story
is that they simply have better vision: because they're so talented, they see
paths that others miss. But if you look at the way great discoveries are made,
that's not what happens. Darwin didn't pay closer attention to individual
species than other people because he saw that this would lead to great
discoveries, and they didn't. He was just really, really interested in such
things.  
  
Darwin couldn't turn it off. Neither could Ramanujan. They didn't discover the
hidden paths that they did because they seemed promising, but because they
couldn't help it. That's what allowed them to follow paths that someone who
was merely ambitious would have ignored.  
  
What rational person would decide that the way to write great novels was to
begin by spending several years creating an imaginary elvish language, like
Tolkien, or visiting every household in southwestern Britain, like Trollope?
No one, including Tolkien and Trollope.  
  
The bus ticket theory is similar to Carlyle's famous definition of genius as
an infinite capacity for taking pains. But there are two differences. The bus
ticket theory makes it clear that the source of this infinite capacity for
taking pains is not infinite diligence, as Carlyle seems to have meant, but
the sort of infinite interest that collectors have. It also adds an important
qualification: an infinite capacity for taking pains about something that
matters.  
  
So what matters? You can never be sure. It's precisely because no one can tell
in advance which paths are promising that you can discover new ideas by
working on what you're interested in.  
  
But there are some heuristics you can use to guess whether an obsession might
be one that matters. For example, it's more promising if you're creating
something, rather than just consuming something someone else creates. It's
more promising if something you're interested in is difficult, especially if
it's _more difficult for other people_ than it is for you. And the obsessions
of talented people are more likely to be promising. When talented people
become interested in random things, they're not truly random.  
  
But you can never be sure. In fact, here's an interesting idea that's also
rather alarming if it's true: it may be that to do great work, you also have
to waste a lot of time.  
  
In many different areas, reward is proportionate to risk. If that rule holds
here, then the way to find paths that lead to truly great work is to be
willing to expend a lot of effort on things that turn out to be every bit as
unpromising as they seem.  
  
I'm not sure if this is true. On one hand, it seems surprisingly difficult to
waste your time so long as you're working hard on something interesting. So
much of what you do ends up being useful. But on the other hand, the rule
about the relationship between risk and reward is so powerful that it seems to
hold wherever risk occurs. _Newton's_ case, at least, suggests that the
risk/reward rule holds here. He's famous for one particular obsession of his
that turned out to be unprecedentedly fruitful: using math to describe the
world. But he had two other obsessions, alchemy and theology, that seem to
have been complete wastes of time. He ended up net ahead. His bet on what we
now call physics paid off so well that it more than compensated for the other
two. But were the other two necessary, in the sense that he had to take big
risks to make such big discoveries? I don't know.  
  
Here's an even more alarming idea: might one make all bad bets? It probably
happens quite often. But we don't know how often, because these people don't
become famous.  
  
It's not merely that the returns from following a path are hard to predict.
They change dramatically over time. 1830 was a really good time to be
obsessively interested in natural history. If Darwin had been born in 1709
instead of 1809, we might never have heard of him.  
  
What can one do in the face of such uncertainty? One solution is to hedge your
bets, which in this case means to follow the obviously promising paths instead
of your own private obsessions. But as with any hedge, you're decreasing
reward when you decrease risk. If you forgo working on what you like in order
to follow some more conventionally ambitious path, you might miss something
wonderful that you'd otherwise have discovered. That too must happen all the
time, perhaps even more often than the genius whose bets all fail.  
  
The other solution is to let yourself be interested in lots of different
things. You don't decrease your upside if you switch between equally genuine
interests based on which seems to be working so far. But there is a danger
here too: if you work on too many different projects, you might not get deeply
enough into any of them.  
  
One interesting thing about the bus ticket theory is that it may help explain
why different types of people excel at different kinds of work. Interest is
much more unevenly distributed than ability. If natural ability is all you
need to do great work, and natural ability is evenly distributed, you have to
invent elaborate theories to explain the skewed distributions we see among
those who actually do great work in various fields. But it may be that much of
the skew has a simpler explanation: different people are interested in
different things.  
  
The bus ticket theory also explains why people are less likely to do great
work after they have children. Here interest has to compete not just with
external obstacles, but with another interest, and one that for most people is
extremely powerful. It's harder to find time for work after you have kids, but
that's the easy part. The real change is that you don't want to.  
  
But the most exciting implication of the bus ticket theory is that it suggests
ways to encourage great work. If the recipe for genius is simply natural
ability plus hard work, all we can do is hope we have a lot of ability, and
work as hard as we can. But if interest is a critical ingredient in genius, we
may be able, by cultivating interest, to cultivate genius.  
  
For example, for the very ambitious, the bus ticket theory suggests that the
way to do great work is to relax a little. Instead of gritting your teeth and
diligently pursuing what all your peers agree is the most promising line of
research, maybe you should try doing something just for fun. And if you're
stuck, that may be the vector along which to break out.  
  
I've always liked _Hamming's_ famous double-barrelled question: what are the
most important problems in your field, and why aren't you working on one of
them? It's a great way to shake yourself up. But it may be overfitting a bit.
It might be at least as useful to ask yourself: if you could take a year off
to work on something that probably wouldn't be important but would be really
interesting, what would it be?  
  
The bus ticket theory also suggests a way to avoid slowing down as you get
older. Perhaps the reason people have fewer new ideas as they get older is not
simply that they're losing their edge. It may also be because once you become
established, you can no longer mess about with irresponsible side projects the
way you could when you were young and no one cared what you did.  
  
The solution to that is obvious: remain irresponsible. It will be hard,
though, because the apparently random projects you take up to stave off
decline will read to outsiders as evidence of it. And you yourself won't know
for sure that they're wrong. But it will at least be more fun to work on what
you want.  
  
It may even be that we can cultivate a habit of intellectual bus ticket
collecting in kids. The usual plan in education is to start with a broad,
shallow focus, then gradually become more specialized. But I've done the
opposite with my kids. I know I can count on their school to handle the broad,
shallow part, so I take them deep.  
  
When they get interested in something, however random, I encourage them to go
preposterously, bus ticket collectorly, deep. I don't do this because of the
bus ticket theory. I do it because I want them to feel the joy of learning,
and they're never going to feel that about something I'm making them learn. It
has to be something they're interested in. I'm just following the path of
least resistance; depth is a byproduct. But if in trying to show them the joy
of learning I also end up training them to go deep, so much the better.  
  
Will it have any effect? I have no idea. But that uncertainty may be the most
interesting point of all. There is so much more to learn about how to do great
work. As old as human civilization feels, it's really still very young if we
haven't nailed something so basic. It's exciting to think there are still
discoveries to make about discovery. If that's the sort of thing you're
interested in.  
  
  
  
  
  
  
  
  
  
  
  
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