Alec Nevala-Lee

Thoughts on art, creativity, and the writing life.

Posts Tagged ‘Hacker News

The next three years

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No matter what your field might be, the most important factor in doing interesting work is often the selection of problems to tackle. We don’t always get to decide how we spend our time from one day to the next, but we occasionally arrive at decision points that will determine what we’ll be doing for years to come. Such moments tend to happen when we aren’t fully prepared for them, like when we have to pick a college major, and even as adults, we frequently fall back on instinct—and if some people have greater success than others, it might just be because they have better hunches. But we don’t always make such choices with the seriousness that they deserve. This might appear to go against the principle that ideas are cheap and execution is what really counts, but they aren’t as inconsistent as they seem. It’s true that there’s a big difference between having a bright idea and actually seeing it through, and that you should worry less about people stealing your ideas than about successfully bringing projects to completion. The world is full of good ideas, and if you lose out on one, there’s always another. But not every idea is equally suited for what you bring to it, and if you choose poorly, it can take you in the wrong direction for years. And it’s often the ideas that seem the most exciting at first that turn out to be the most misleading. (If I seem particularly interested in the subject right now, it’s because I’m about to deliver what I expect will effectively be the final draft of my book Astounding. The next few months will be taken up by the practical side of book publication, and I really need a break. But at some point, I’m going to have to figure out what to do next. And I’m writing this post to set down some guidelines for my future self about where to look.)

Not surprisingly, this issue gets a lot of attention in science and technology, which are fields in which the choice of subject can be crucial. In Advice for a Young Scientist, Peter Medawar has an entire chapter titled “What Should I Research?”, and he offers a good place to start:

It can be said with complete confidence that any scientist of any age who wants to make important discoveries must study important problems. Dull or piffling problems yield dull or piffling answers. It is not enough that a problem be “interesting”—almost any problem is interesting if it is studied in sufficient depth…In choosing topics for research and departments to enlist in, a young scientist must beware of following fashion. It is one thing to fall into step with a great concerted movement of thought such as molecular genetics or cellular immunology, but quite another merely to fall in love with prevailing fashion for, say, some new histochemical procedure or chemical gimmick.

In his fascinating, sometimes infuriating memoir Avoid Boring People, James D. Watson makes a similar point: “Mopping up the details after a major discovery has been made by others will not likely make you out as an important scientist. Better to leapfrog ahead of your peers by pursuing an important objective that most others feel is not for the current moment.” But he also qualifies this in a way that seems worth remembering:

I feel comfortable taking on a problem only when I believe meaningful results can come over a three-to-five-year interval. Risking your career on problems when you have any a tiny chance to see a finish line is not advisable. But if you have reason to believe you have a thirty percent chance of solving over the next two or three years a problem that most others feel is not for this decade, that’s a shot worth taking.

Watson knows what he’s talking about, but his own claim to fame—the discovery of the structure of DNA—was also due in part to luck and good timing. As Max Perutz, who won a Nobel Prize for his work on hemoglobin, recalled:

I sometimes envied Jim. My own problem took thousands of hours of hard work, measurements, calculations. I often thought that there must be some way to cut through it—that there must be, if only I could see it, an elegant solution. There wasn’t any. For Jim’s there was an elegant solution, which is what I admired. He found it partly because he never made the mistake of confusing hard work with hard thinking; he always refused to substitute one for the other.

Success, in other words, doesn’t just depend on choosing an important subject, but finding one in which you might hold an advantage. As Herbert A. Simon put it so memorably:

I advise my graduate students to pick a research problem that is important (so that it will matter if it is solved), but one for which they have a secret weapon that gives some prospect of success. Why a secret weapon? Because if the problem is important, other researchers as intelligent as my students will be trying to solve it; my students are likely to come in first only by having access to some knowledge or research methods the others do not have…In reviewing the record, I observe that I have always been pretty careful in setting the odds, and have usually behaved like an honest professional gambler…It is not unfair to have the experiences or to be at the places that provide one with a secret weapon.

Such weapons aren’t always obvious, and recognizing them can require a genius of its own. (For example, Simon writes that one of his secret weapons in the fifties was “a digital computer, and an idea—derived from contact with computers—that it would be used as a general processor of symbols,” which is hardly a trivial insight.) I’ve said elsewhere that I like to focus on areas where information is “available, but obscure,” and I often find myself thinking of an anonymous comment on a thread on Hacker News:

Find an unsexy domain that you have more access to than the average person. Start to build domain expertise in that area as quickly as you can (people are surprisingly willing to talk when you don’t want to sell them something, but just learn about how they do things)…Loop back with the people in the unsexy industry to get feedback. Remember, not all industries are bombarded with technology—you’ll need to strike a balance between showing them something sufficiently “fancy” to pique interest, and abstracting away your technology so they focus on a problem it solves…Build things in a low-cost way and use that to identify tangentially related problems until you think you’ve found a big enough pain point.

That’s basically how I wrote my book, and I’ve since come to realize how lucky I was to choose a subject that was neglected enough for me to do something useful and new, while also interesting enough to open doors. Frankly, I’m not sure if I’ll ever be able to do it again, although I’ll be thinking hard about how. I’ll make the best choice that I can. And I’ll know whether or not I was right in about three years.

Written by nevalalee

March 2, 2018 at 8:44 am

Live from Silicon Valley

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Last week, on an impulse, I picked up a used copy of Live From New York by Tom Shales and James Andrew Miller, an oral history of Saturday Night Live that came out more than fifteen years ago. I honestly don’t know why it took me so long to get to it—it’s a fantastic read, particularly if you allow yourself to browse at random, and it seems to have singlehandedly kicked off the oral history boom that has become pervasive enough to be the object of satire itself. There are countless anecdotes that I’d love to turn into the subject of a post, but I’ll start with this one, from legendary comedy writer James Downey:

Lorne [Michaels] at the time was anxious to get into movies in a big way, and he had a deal with Paramount. And different writers and teams of writers—like Tom Schiller wrote a movie—each had movie ideas. Lorne was pushing [Al] Franken and [Tom] Davis and myself the most to do a movie. But we didn’t really have an idea. We had the deal before we had the idea, which is not a good way to do anything. So from like the summer of 1980 on and off for the next two years, we just in a desultory way wrote the screenplay, which once we finished it Paramount was then able to officially reject.

The italics are mine. And while it’s tempting to agree that you should start with the idea, that’s often not how it works in Hollywood. Instead, like Michaels, you get a development deal, which amounts to a bet by a studio that you’re talented enough to eventually come up with something interesting.

And you don’t just see this in the entertainment industry. Yesterday, my wife brought my attention to a post on Hacker News with the title “We have a great team and capital but can’t find a good idea.” The poster noted that he had a group consisting of himself and two friends, one with a lot of money from a stint in private equity, the other with a doctorate in computer science. They had “investors that are willing to write blank checks” and “cash in the bank to continue experimenting,” but they were missing one crucial element. The poster elaborated:

We have read everything on how to come up with startup ideas (ranging from Paul Graham essays to The Mom Test). We have ran interviews with friends in corporate and startups, asked old colleagues, attended conferences, organized meetups in our city, a ton of time spent networking, etc. The few product ideas we came up with following the above process we dropped, often because we discovered that that space is ultra crowded or commoditized. We will not give up but are getting unsure on how to break the stalemate. Any tips or advice?

The suggestions, not surprisingly, ranged from “stop looking for ideas and…start looking for problems” to hiring an “idea generator” to getting out of the game entirely. (My favorite: “Find an unsexy domain that you have more access to than the average person. Start to build domain expertise in that area as quickly as you can…Loop back with the people in the unsexy industry to get feedback.” I like this because it’s basically how I wrote my book.)

It’s easy to smile at this sort of thing, but it reflects an assumption that still permeates much of Silicon Valley, which is that what matters isn’t the idea, but the team. Hacker News is an affiliate of the startup incubator Y Combinator, which essentially provides development deals for promising entrepreneurs, with a business philosophy to match. In his book The Launch Pad, Randall Stross says of its cofounder Paul Graham: “Graham is much more interested in the founders than in the proposed business idea. When he sees a strong team of founders with the qualities that he believes favor success, he will overlook a weak idea.” Elsewhere, Graham himself has written:

The fact is, most startups end up nothing like the initial idea. It would be closer to the truth to say the main value of your initial idea is that, in the process of discovering it’s broken, you’ll come up with your real idea…Since a startup ought to have multiple founders who were already friends before they decided to start a company, the rather surprising conclusion is that the best way to generate startup ideas is to do what hackers do for fun: cook up amusing hacks with your friends.

And the notion that the team itself is what truly counts has led to a lot of talk, legitimate or otherwise, about the concept of the pivot, in which a startup that began by doing one thing abruptly decides to do something else.

In fact, the underlying point here seems sound enough. Ideas are cheap, and incubators are probably right in investing in founders rather than in concepts. If I had the money to be a venture capitalist, I’d do the same thing. But in the end, the real test of the team is its ability to generate and execute a good idea. (Most people who get development deals of any kind have already managed to do it at least once.) And you only get the tools that you need to do anything well by coming up with ideas on your own and taking them as far as you can. Just as you can learn vastly more from writing a novel from scratch than from fanfic or ghostwriting somebody else’s book, shepherding an idea to start to finish is the most reliable way of developing certain indispensable skills. As Chris Rock says in Live from New York:

The best thing about the show is that when you did write a piece, you were responsible for it. You were in charge of the casting. You were in charge of the costumes. You produced the piece. I wouldn’t know what the fuck I was doing if I hadn’t been on Saturday Night Live. It’s the absolute best training you can have in show business.

You could say much the same thing about any project, as long as you see it to the end. Its lifespan may not be any longer than that of your average comedy sketch, but its lessons remain—which is just another way of saying that ideas and experience emerge from the same cycle. And the apprenticeship is necessarily brutal, in Silicon Valley or anywhere else. As Martin Short puts it elsewhere in the same book: “You’re a star on Saturday night, but if forty-eight hours later you haven’t come up with an idea, you’re a failure.”

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