Invention, influence, and impact

A few months ago, at a conference dinner filled with academics and founders, my table-mates were gamely trying to understand my work. One asked: what am I aiming for with my output? Am I trying to influence others—e.g. by publishing, like the academics? Or am I working towards practical impact—e.g. by making ideas directly usable, like the founders?

Somewhat petulantly, I replied that I’m mostly aiming for the transcendent satisfaction of creation. There’s an expressive element to the work. I have some instinctive yearning; I want things to be otherwise in some particular way. It’s extremely gratifying to condense an idea from the ether which manifests those impulses. There’s also a real thrill of discovery. There’s a meaningful pattern hiding in the texture of reality; I’ve traced its seams, made it dance.

But my answer wasn’t quite true. If I had all that creative joy in a secluded cabin, permanently disconnected from the outside world, I wouldn’t be satisfied. I want to help bring alien cognitive and creative powers into the world—not just into my own imagination. If my ideas don’t eventually become widely usable, that doesn’t seem like success. It seems more like carefully planting a beautiful orchard, then failing to water it. Or like watching those trees grow, then discovering that they can’t survive the local climate after all. Neither outcome would be gratifying.

These answers highlight a difficult tension. The work I find most satisfying focuses on invention and discovery. Yet invention and discovery aren’t enough. I want my ideas to impact people’s lives—which involves a great deal of a very different kind of work. As I look back at this year and plan the new one, I’m wondering anew: what should I be aiming for with my output? What is my theory of change?

SuperMemo and Sketchpad

Consider SuperMemo, the first computational spaced repetition system. In practical impact, it has been largely eclipsed by Anki and Duolingo. But SuperMemo got the ball rolling. I’d be very satisfied if I were its inventor, Piotr Wozniak.

SuperMemo began with a few years of paper prototypes as part of Wozniak’s masters thesis. Then in 1987, he implemented a simple initial version in DOS that he and his friends could use. Wozniak wasn’t entrepreneurially minded, but two of his schoolmates were. They would eventually develop and market SuperMemo to the world. If Wozniak had stopped with his master’s thesis and those early prototypes, I don’t think that Anki, the mnemonic medium, or any other modern memory system would exist. It’s true that the testing effect and spacing effect are widely studied in educational psychology, but to this day there has been little effort to translate those effects outside the approach that Wozniak established. I would not be satisfied as this alternate-world Wozniak, with the system deployed only to me and a few friends.

Consider Sketchpad, Ivan Sutherland’s groundbreaking 1963 CAD system, and the first realtime interactive GUI. It was his PhD thesis. Sutherland didn’t develop or market Sketchpad much further. But I’d certainly be satisfied if I were in his shoes. Sketchpad was wildly influential. It’s one of the most important works in the history of personal computing.

What’s the difference here? Why was merely creating a prototype and publishing about it enough for Sketchpad, but not for SuperMemo? One answer is that Sketchpad’s ideas were much more general, and they slotted nicely into a swell of activity which was already taking place. Another answer is that Sutherland was at the MIT Lincoln Laboratory, along with many of the best minds in computing. He was supervised by Claude Shannon and Marvin Minsky. Meanwhile, Wozniak wrote his thesis at a Polish university where it was hard for him to regularly access a computer—the impoverished country was struggling under communist rule.

These examples illustrate that if my theory of change centers on influence, my success will depend a great deal on my environment, on who’s getting influenced, and on synergy between our work.

Latticework and Quantum Country

Consider Latticework, the augmented sensemaking system that Matthew Siu and I published earlier this year. That work isn’t Sketchpad or SuperMemo, by any means—but I’m proud of it, and I’d like to see its ideas get into people’s hands. Latticework hasn’t yet been terribly influential. I don’t think that’s because of the quality of its ideas: they have limitations, but other more limited designs have gotten more attention.

I think the main problem is that it’s not real enough. We built a prototype, but its edges are very rough, so we put it in a footnote and haven’t encouraged people to use it. If we want those ideas to go anywhere, the people we need to influence are mostly the kind of tinkerers who will be motivated by something they can get their hands on. That doesn’t mean our article is useless: if one of those tinkerers was inspired to improve upon our prototype, they’d benefit enormously from all that background thought and explanation. But we have to get someone to that point first.

Quantum Country makes for a good contrast. It presents a new idea in a tightly-scoped context. It’s easy to try the system out and get a feel for its potential. And if you’re interested in the more elaborate design thinking behind the system, we made that available too. Quantum Country has been relatively influential—at least half a dozen founders have told me that their projects were inspired by it. I think the system’s tangibility has been key to its relative success.

A lesson I take here is that my systems are much more likely to be influential if they’re instantiated in a prototype that people can meaningfully use.

Quantum Country and Orbit

Quantum Country also illustrates an anti-pattern for my work. Since the mnemonic medium seemed to be working well, I wondered: does this generalize? Can I apply these ideas to a wide range of texts? So I built Orbit, a generalized platform for the mnemonic medium. Then I built tools so that authors can easily add Quantum Country’s interleaved flashcards to any online book.

This was a mistake. Once I had the system working, and once I’d built relationships with authors to write a few texts using it, it didn’t take long to find serious flaws in the core design of the mnemonic medium. But because I pushed to generalize, it took me a year to get to that point. I could have identified those problems in a fraction of the time if I’d just built another one-off or two like Quantum Country.

I think this was a matter of absorbing too much San Francisco culture. As Michael Nielsen has put it to me, there’s an oppressive “cloud of people wanting startup answers to questions.” I wasn’t thinking about a startup, but I was thinking about scale, about generality, about “platforms”. It meant a lot of wasted effort, and technical debt that I still carry.

A lesson I take here is that I must carefully separate the tasks of discovery, influence, and impact. Quantum Country was neatly self-contained and legible enough to influence people. It was a one-off, so it could never have direct impact—but figuring out how to generalize it was a problem of discovery which, by building scalable infrastructure, I approached with the tools of impact.

When to build for impact?

Suppose that I followed my own advice, and I built one-offs to discover the various problems with generalizing the mnemonic medium. Then suppose I built new prototypes which solved those problems in a legible and influential way, like Quantum Country. What then? Would I want to switch to building generalized infrastructure?

My instinct is to try hard to get the impact I want without doing that. I sympathize with Kevin Kelly’s policy: try hard to give away an idea—to get others to pursue it—before committing to it myself. I’ve built mass-market products before. That work often has little in common with the practice of discovery and invention that I find so rewarding, and that I can more uniquely do. My ideal would be to give a concept just enough clarity and momentum that it takes on a life of its own, with the help of others of course, and snowballs into something impactful.

I can imagine exceptions, of course. If I’m convinced that I’ve invented something transformative, but no one’s deploying it properly, I may need to push it over the finish line myself. Some ideas—like a social network—can’t really be properly explored without lots of production work. Some ideas—like Edison’s power grid—are about scaling, and so can only be developed in the context of scaling. And maybe, for the right idea and the right group of people, building a version for the world might seem so fun that I’d be happy to dive in despite my usual preferences.

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Thanks to Taylor Rogalski for a suggestion congruent to the “cabin in the woods” thought experiment in the introduction.