October 2020  
  
One of the biggest things holding people back from doing great work is the
fear of making something lame. And this fear is not an irrational one. Many
great projects go through a stage early on where they don't seem very
impressive, even to their creators. You have to push through this stage to
reach the great work that lies beyond. But many people don't. Most people
don't even reach the stage of making something they're embarrassed by, let
alone continue past it. They're too frightened even to start.  
  
Imagine if we could turn off the fear of making something lame. Imagine how
much more we'd do.  
  
Is there any hope of turning it off? I think so. I think the habits at work
here are not very deeply rooted.  
  
Making new things is itself a new thing for us as a species. It has always
happened, but till the last few centuries it happened so slowly as to be
invisible to individual humans. And since we didn't need customs for dealing
with new ideas, we didn't develop any.  
  
We just don't have enough experience with early versions of ambitious projects
to know how to respond to them. We judge them as we would judge more finished
work, or less ambitious projects. We don't realize they're a special case.  
  
Or at least, most of us don't. One reason I'm confident we can do better is
that it's already starting to happen. There are already a few places that are
living in the future in this respect. Silicon Valley is one of them: an
unknown person working on a strange-sounding idea won't automatically be
dismissed the way they would back home. In Silicon Valley, people have learned
how dangerous that is.  
  
The right way to deal with new ideas is to treat them as a challenge to your
imagination � not just to have lower standards, but to [_switch
polarity_](altair.html) entirely, from listing the reasons an idea won't work
to trying to think of ways it could. That's what I do when I meet people with
new ideas. I've become quite good at it, but I've had a lot of practice. Being
a partner at Y Combinator means being practically immersed in strange-sounding
ideas proposed by unknown people. Every six months you get thousands of new
ones thrown at you and have to sort through them, knowing that in a world with
a power-law distribution of outcomes, it will be painfully obvious if you miss
the needle in this haystack. Optimism becomes urgent.  
  
But I'm hopeful that, with time, this kind of optimism can become widespread
enough that it becomes a social custom, not just a trick used by a few
specialists. It is after all an extremely lucrative trick, and those tend to
spread quickly.  
  
Of course, inexperience is not the only reason people are too harsh on early
versions of ambitious projects. They also do it to seem clever. And in a field
where the new ideas are risky, like startups, those who dismiss them are in
fact more likely to be right. Just not when their predictions are [_weighted
by outcome_](swan.html).  
  
But there is another more sinister reason people dismiss new ideas. If you try
something ambitious, many of those around you will hope, consciously or
unconsciously, that you'll fail. They worry that if you try something
ambitious and succeed, it will put you above them. In some countries this is
not just an individual failing but part of the national culture.  
  
I wouldn't claim that people in Silicon Valley overcome these impulses because
they're morally better. [1] The reason many hope you'll succeed is that they
hope to rise with you. For investors this incentive is particularly explicit.
They want you to succeed because they hope you'll make them rich in the
process. But many other people you meet can hope to benefit in some way from
your success. At the very least they'll be able to say, when you're famous,
that they've known you since way back.  
  
But even if Silicon Valley's encouraging attitude is rooted in self-interest,
it has over time actually grown into a sort of benevolence. Encouraging
startups has been practiced for so long that it has become a custom. Now it
just seems that that's what one does with startups.  
  
Maybe Silicon Valley is too optimistic. Maybe it's too easily fooled by
impostors. Many less optimistic journalists want to believe that. But the
lists of impostors they cite are suspiciously short, and plagued with
asterisks. [2] If you use revenue as the test, Silicon Valley's optimism seems
better tuned than the rest of the world's. And because it works, it will
spread.  
  
There's a lot more to new ideas than new startup ideas, of course. The fear of
making something lame holds people back in every field. But Silicon Valley
shows how quickly customs can evolve to support new ideas. And that in turn
proves that dismissing new ideas is not so deeply rooted in human nature that
it can't be unlearnt.  
  
___________  
  
Unfortunately, if you want to do new things, you'll face a force more powerful
than other people's skepticism: your own skepticism. You too will judge your
early work too harshly. How do you avoid that?  
  
This is a difficult problem, because you don't want to completely eliminate
your horror of making something lame. That's what steers you toward doing good
work. You just want to turn it off temporarily, the way a painkiller
temporarily turns off pain.  
  
People have already discovered several techniques that work. Hardy mentions
two in _A Mathematician's Apology_ :

> Good work is not done by "humble" men. It is one of the first duties of a
> professor, for example, in any subject, to exaggerate a little both the
> importance of his subject and his importance in it.

If you overestimate the importance of what you're working on, that will
compensate for your mistakenly harsh judgment of your initial results. If you
look at something that's 20% of the way to a goal worth 100 and conclude that
it's 10% of the way to a goal worth 200, your estimate of its expected value
is correct even though both components are wrong.  
  
It also helps, as Hardy suggests, to be slightly overconfident. I've noticed
in many fields that the most successful people are slightly overconfident. On
the face of it this seems implausible. Surely it would be optimal to have
exactly the right estimate of one's abilities. How could it be an advantage to
be mistaken? Because this error compensates for other sources of error in the
opposite direction: being slightly overconfident armors you against both other
people's skepticism and your own.  
  
Ignorance has a similar effect. It's safe to make the mistake of judging early
work as finished work if you're a sufficiently lax judge of finished work. I
doubt it's possible to cultivate this kind of ignorance, but empirically it's
a real advantage, especially for the young.  
  
Another way to get through the lame phase of ambitious projects is to surround
yourself with the right people � to create an eddy in the social headwind. But
it's not enough to collect people who are always encouraging. You'd learn to
discount that. You need colleagues who can actually tell an ugly duckling from
a baby swan. The people best able to do this are those working on similar
projects of their own, which is why university departments and research labs
work so well. You don't need institutions to collect colleagues. They
naturally coalesce, given the chance. But it's very much worth accelerating
this process by seeking out other people trying to do new things.  
  
Teachers are in effect a special case of colleagues. It's a teacher's job both
to see the promise of early work and to encourage you to continue. But
teachers who are good at this are unfortunately quite rare, so if you have the
opportunity to learn from one, take it. [3]  
  
For some it might work to rely on sheer discipline: to tell yourself that you
just have to press on through the initial crap phase and not get discouraged.
But like a lot of "just tell yourself" advice, this is harder than it sounds.
And it gets still harder as you get older, because your standards rise. The
old do have one compensating advantage though: they've been through this
before.  
  
It can help if you focus less on where you are and more on the rate of change.
You won't worry so much about doing bad work if you can see it improving.
Obviously the faster it improves, the easier this is. So when you start
something new, it's good if you can spend a lot of time on it. That's another
advantage of being young: you tend to have bigger blocks of time.  
  
Another common trick is to start by considering new work to be of a different,
less exacting type. To start a painting saying that it's just a sketch, or a
new piece of software saying that it's just a quick hack. Then you judge your
initial results by a lower standard. Once the project is rolling you can
sneakily convert it to something more. [4]  
  
This will be easier if you use a medium that lets you work fast and doesn't
require too much commitment up front. It's easier to convince yourself that
something is just a sketch when you're drawing in a notebook than when you're
carving stone. Plus you get initial results faster. [5] [6]  
  
It will be easier to try out a risky project if you think of it as a way to
learn and not just as a way to make something. Then even if the project truly
is a failure, you'll still have gained by it. If the problem is sharply enough
defined, failure itself is knowledge: if the theorem you're trying to prove
turns out to be false, or you use a structural member of a certain size and it
fails under stress, you've learned something, even if it isn't what you wanted
to learn. [7]  
  
One motivation that works particularly well for me is curiosity. I like to try
new things just to see how they'll turn out. We started Y Combinator in this
spirit, and it was one of main things that kept me going while I was working
on [_Bel_](bel.html). Having worked for so long with various dialects of Lisp,
I was very curious to see what its inherent shape was: what you'd end up with
if you followed the axiomatic approach all the way.  
  
But it's a bit strange that you have to play mind games with yourself to avoid
being discouraged by lame-looking early efforts. The thing you're trying to
trick yourself into believing is in fact the truth. A lame-looking early
version of an ambitious project truly is more valuable than it seems. So the
ultimate solution may be to teach yourself that.  
  
One way to do it is to study the histories of people who've done great work.
What were they thinking early on? What was the very first thing they did? It
can sometimes be hard to get an accurate answer to this question, because
people are often embarrassed by their earliest work and make little effort to
publish it. (They too misjudge it.) But when you can get an accurate picture
of the first steps someone made on the path to some great work, they're often
pretty feeble. [8]  
  
Perhaps if you study enough such cases, you can teach yourself to be a better
judge of early work. Then you'll be immune both to other people's skepticism
and your own fear of making something lame. You'll see early work for what it
is.  
  
Curiously enough, the solution to the problem of judging early work too
harshly is to realize that our attitudes toward it are themselves early work.
Holding everything to the same standard is a crude version 1. We're already
evolving better customs, and we can already see signs of how big the payoff
will be.  
  
  
  
  
  
  
  
  
  
**Notes**  
  
[1] This assumption may be too conservative. There is some evidence that
historically the Bay Area has attracted a [_different sort of
person_](cities.html) than, say, New York City.  
  
[2] One of their great favorites is Theranos. But the most conspicuous feature
of Theranos's cap table is the absence of Silicon Valley firms. Journalists
were fooled by Theranos, but Silicon Valley investors weren't.  
  
[3] I made two mistakes about teachers when I was younger. I cared more about
professors' research than their reputations as teachers, and I was also wrong
about what it meant to be a good teacher. I thought it simply meant to be good
at explaining things.  
  
[4] Patrick Collison points out that you can go past treating something as a
hack in the sense of a prototype and onward to the sense of the word that
means something closer to a practical joke:

> I think there may be something related to being a hack that can be powerful
> � the idea of making the tenuousness and implausibility _a feature_. "Yes,
> it's a bit ridiculous, right? I'm just trying to see how far such a naive
> approach can get." YC seemed to me to have this characteristic.

[5] Much of the advantage of switching from physical to digital media is not
the software per se but that it lets you start something new with little
upfront commitment.  
  
[6] John Carmack adds:

> The value of a medium without a vast gulf between the early work and the
> final work is exemplified in game mods. The original Quake game was a golden
> age for mods, because everything was very flexible, but so crude due to
> technical limitations, that quick hacks to try out a gameplay idea weren't
> all _that_ far from the official game. Many careers were born from that, but
> as the commercial game quality improved over the years, it became almost a
> full time job to make a successful mod that would be appreciated by the
> community. This was dramatically reversed with Minecraft and later Roblox,
> where the entire esthetic of the experience was so explicitly crude that
> innovative gameplay concepts became the overriding value. These "crude" game
> mods by single authors are now often bigger deals than massive professional
> teams' work.

[7] Lisa Randall suggests that we

> treat new things as experiments. That way there's no such thing as failing,
> since you learn something no matter what. You treat it like an experiment in
> the sense that if it really rules something out, you give up and move on,
> but if there's some way to vary it to make it work better, go ahead and do
> that

[8] Michael Nielsen points out that the internet has made this easier, because
you can see programmers' first commits, musicians' first videos, and so on.  
  
  
  
**Thanks** to Trevor Blackwell, John Carmack, Patrick Collison, Jessica
Livingston, Michael Nielsen, and Lisa Randall for reading drafts of this.  
  

