How to Do Great Work -->
July 2023
If you collected lists of techniques for doing great work in a lot<br>of different fields, what would the intersection look like? I decided<br>to find out by making it.
Partly my goal was to create a guide that could be used by someone<br>working in any field. But I was also curious about the shape of the<br>intersection. And one thing this exercise shows is that it does<br>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<br>needs to have three qualities: it has to be something you have a<br>natural aptitude for, that you have a deep interest in, and that<br>offers scope to do great work.
In practice you don't have to worry much about the third criterion.<br>Ambitious people are if anything already too conservative about it.<br>So all you need to do is find something you have an aptitude for<br>and great interest in.<br>[1]
That sounds straightforward, but it's often quite difficult. When<br>you're young you don't know what you're good at or what different<br>kinds of work are like. Some kinds of work you end up doing may not<br>even exist yet. So while some people know what they want to do at<br>14, most have to figure it out.
The way to figure out what to work on is by working. If you're not<br>sure what to work on, guess. But pick something and get going.<br>You'll probably guess wrong some of the time, but that's fine. It's<br>good to know about multiple things; some of the biggest discoveries<br>come from noticing connections between different fields.
Develop a habit of working on your own projects. Don't let "work"<br>mean something other people tell you to do. If you do manage to do<br>great work one day, it will probably be on a project of your own.<br>It may be within some bigger project, but you'll be driving your<br>part of it.
What should your projects be? Whatever seems to you excitingly<br>ambitious. As you grow older and your taste in projects evolves,<br>exciting and important will converge. At 7 it may seem excitingly<br>ambitious to build huge things out of Lego, then at 14 to teach<br>yourself calculus, till at 21 you're starting to explore unanswered<br>questions in physics. But always preserve excitingness.
There's a kind of excited curiosity that's both the engine and the<br>rudder of great work. It will not only drive you, but if you let<br>it have its way, will also show you what to work on.
What are you excessively curious about — curious to a degree that<br>would bore most other people? That's what you're looking for.
Once you've found something you're excessively interested in, the<br>next step is to learn enough about it to get you to one of the<br>frontiers of knowledge. Knowledge expands fractally, and from a<br>distance its edges look smooth, but once you learn enough to get<br>close to one, they turn out to be full of gaps.
The next step is to notice them. This takes some skill, because<br>your brain wants to ignore such gaps in order to make a simpler<br>model of the world. Many discoveries have come from asking questions<br>about things that everyone else took for granted.<br>[2]
If the answers seem strange, so much the better. Great work often<br>has a tincture of strangeness. You see this from painting to math.<br>It would be affected to try to manufacture it, but if it appears,<br>embrace it.
Boldly chase outlier ideas, even if other people aren't interested<br>in them — in fact, especially if they aren't. If you're excited<br>about some possibility that everyone else ignores, and you have<br>enough expertise to say precisely what they're all overlooking,<br>that's as good a bet as you'll find.<br>[3]
Four steps: choose a field, learn enough to get to the frontier,<br>notice gaps, explore promising ones. This is how practically everyone<br>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<br>to prove that you have to work hard to do great things, but the<br>empirical evidence is on the scale of the evidence for mortality.<br>That's why it's essential to work on something you're deeply<br>interested in. Interest will drive you to work harder than mere<br>diligence ever could.
The three most powerful motives are curiosity, delight, and the<br>desire to do something impressive. Sometimes they converge, and<br>that combination is the most powerful of all.
The big prize is to discover a new fractal bud. You notice a crack<br>in the surface of knowledge, pry it open, and there's a whole world<br>inside.
Let's talk a little more about the complicated business of figuring<br>out what to work on. The main reason it's hard is that you can't<br>tell what most kinds of work are like except by doing them. Which<br>means the four steps overlap: you may have to work at something for<br>years before you know how much you like it or how good you are at<br>it. And in the meantime you're not doing, and thus not learning<br>about, most other kinds of work. So in the worst case you choose<br>late based on very...