Timing Technology: Lessons From The Media Lab

The question constantly asked of anyone who claims to know a better way (as futurologists implicitly do): “If you’re so smart, why aren’t you rich?” The lesson I draw is: it is not enough to predict the future, one has to get the timing right to not be ruined, and then execute, and then get lucky in a myriad ways.

Many ‘bubbles’ can be interpreted as people being 100% correct the future—but missing the timing (Thiel’s article on China and bubbles, The Economist on obscure property booms, Garber’s Famous First Bubbles). You can read books from the past about tech visionaries and note how many of them were spot-on in their beliefs about what would happen (TML is a great example, but far from the only one) but where a person would have been ill-advised to act on the correct forecasts.

Many startups have a long list of failed predecessors who tried to do much the same thing, often simultaneous with several other competitors (startups are just as susceptible to multiple discovery as science/technology in general). What made them a success was that they happened to give the pinata a whack at the exact moment where some S-curves or events hit the right point. Consider the ill-fated eToys.com or Pets.com: was the investor right to believe that Americans would spend a ton of money online such as for buying toys or dogfood? Absolutely, Amazon (which has rarely turned a profit and has sucked up far more investment than Pets.com ever did, a mere ~$559.8^$300₂₀₀₂m) is a successful online retail business that stocks thousands of dog food varieties, to say nothing of all the other pet-related goods it sells, and Chewy, which primarily does pet food, filed for a multi-billion-dollar IPO in 2019 on the strength of its billions in revenue (swelling to a market cap of $37.33^$30₂₀₂₁b mid-2021). But the value of Pets.com stock still went to ~$0. Facebook is the biggest archive of photographs there has ever been, with truly colossal storage requirements; could it have succeeded in the 1990s? No, and not even later, as demonstrated by Orkut and Friendster, and the lingering death of MySpace. One of the most notorious tech business failures of the 1990s was the Iridium satellite constellation, but that was brought down by bizarrely self-sabotaging decisions on the part of Motorola, and when Motorola was finally removed from the equation, Iridium found its market, and 2017 saw the launch of the second Iridium satellite constellation, Iridium NEXT, with competition from other since-launched satellite constellations, including SpaceX’s own nascent Starlink (aiming at global broadband Internet) which launched no less than 60 satellites in May 2019. Or look at computers: imagine an early adopter of an Apple computer saying ‘everyone will use computers eventually!’ Yes, but not for another few decades, and ‘in the long run, we are all dead’. Early PC history is rife with examples of the prescient failing.

Smartphones are an even bigger example of this. How often did I read in the ’90s and early ’00s about how amazing Japanese cellphones were and how amazing a good smartphone would be, even though year after year the phones were jokes and used pretty much solely for voice? You can see the smartphones come up again and again in TML, as the visionaries realize how transformative a mobile pocket-sized computer would be. Yet, it took until the mid-00s for the promise of smartphones to materialize overnight, as it were, a success which went primarily to latecomers Apple and Google, cutting out the previously highly-successful Nokia, never mind visionaries like General Magic. (You too can achieve overnight success in just a few decades of hard work…) A 2013_13ya interview with Eric Jackson looks back on smartphone adoption rates:

Q: “What’s your take on how they’re [Apple] handling their expansion into China, India, and other emerging markets?”

A: “It’s depressing how slow things are moving on that front. We can draw lines on a graph but we don’t know the constraints. Again, the issue with adoption is that the timing is so damn hard. I was expecting smartphones to take off in mid 2004_22ya and was disappointed over and over again. And then suddenly a catalyst took hold and the adoption skyrocketed. Cook calls this ‘cracking the nut’. I don’t know what they can do to move faster but I suspect it has to do with placement (distribution) and with networks which both depend on (corrupt) entities.”

In 2012_14ya, I watched impressed as my aunt used the iPhone application FaceTime to video chat with her daughter half a continent away. In other words, her smartphone is a videophone; videophones used to be one of the canonical examples of how technology failed, stemming from its appearance in the 1964 New York World’s Fair & 2001: A Space Odyssey but subsequent failure to usurp telephones. This was oft-cited as an example of how technoweenies failed to understand that people didn’t really want videophones at all—‘who wants to put on makeup before making a call?’, people offered as an explanation, in all seriousness—but really, it looks like the videophones back then simply weren’t good enough.

Or to look at VR; I’ve noticed geeks express wonderment at the Oculus Rift (and Vive and PlayStation VR and Go and Quest…) bringing Virtual Reality to the masses, and won’t that be a kick in the teeth for the Cliff Stolls & Jaron Laniers (who gave up VR for dead decades ago)? The Verge’s 2012_14ya article on VR took a historical look back at the many failed past efforts, and what’s striking is that VR was clearly foreseen back in the 1950s, before so many other things like the Internet, more than half a century before the computing power or monitors were remotely close to what we now know was needed for truly usable VR. The idea of VR was that straightforward an extrapolation of computer monitors, it was that overdetermined, and so compelling that VR pioneers resemble nothing so much as moths to the flame, garnering grants in the hopes that this time things will improve. And at some point, it does improve, and the first person to try at the right time may win the lottery; Palmer Luckey (founder of Oculus, sold to Facebook for $3.4^$2.3₂₀₁₄ billion in March 2014):

Here’s a secret: the thing stopping people from making good VR and solving these problems was not technical. Someone could have built the Rift in mid-to-late 2007_19ya for a few thousand dollars, and they could have built it in mid-2008 for about $777.66^$500₂₀₀₈. It’s just nobody was paying attention to that.

Any good idea can be made to sound like a bad idea & probably did sound like a bad idea then, and Bessemer VC’s anti-profile is a list of good ideas which Bessemer declined to invest in. Michael Wolfe offers some examples of this:

• Facebook: the world needs yet another MySpace or Friendster [or PlanetAll or…] except several years late. We’ll only open it up to a few thousand overworked, anti-social, Ivy Leaguers. Everyone else will then join since Harvard students are so cool.

• Dropbox: we are going to build a file sharing and syncing solution when the market has a dozen of them that no one uses, supported by big companies like Microsoft. It will only do one thing well, and you’ll have to move all of your content to use it.

• Virgin Atlantic: airlines are cool. Let’s start one. How hard could it be? We’ll differentiate with a funny safety video and by not being a—holes.

• …iOS: a brand new operating system that doesn’t run a single one of the millions of applications that have been developed for Mac OS, Windows, or Linux. Only Apple can build apps for it. It won’t have cut and paste.

• Google: we are building the world’s 20^th search engine at a time when most of the others have been abandoned as being commoditized money losers. We’ll strip out all of the ad-supported news and portal features so you won’t be distracted from using the free search stuff.

• Tesla: instead of just building batteries and selling them to Detroit, we are going to build our own cars from scratch plus own the distribution network. During a recession and a cleantech backlash.

• …Firefox: we are going to build a better web browser, even though 90% of the world’s computers already have a free one built in. One guy will do most of the work.

We can play this game all day:

• How about Netflix? “We’ll start off renting people a doomed format in a way inferior to our established competitor Blockbuster (which will choose to commit suicide by ignoring both mail order & Internet all the way until bankruptcy in 2010); this will (somehow) let us pivot to streaming, where we will license all our content from our worst enemies, who will destroy us the instant we are too successful & already intend to run streaming services of their own—but that’s OK because we’ll just convince Wall Street to wait decades while giving us hundreds of billions of dollars to replace Hollywood by making thousands of film & TV series ourselves (despite the fact that we’ve never done anything like that before and there is no reason to think we would be any better at it than they are).”

• Or Github: “We’ll offer code hosting services like that of SourceForge or Google Code which requires developers to use one of the most user-hostile DVCSes, only to FLOSS developers who are notorious cheapskates, and charge them a few bucks for a private version.”

• SpaceX: “Orbital Sciences Corporation has a multi-decade headstart but are fat and lazy; we’ll catch up by buying some spare Russian rockets while we invent our own futuristic reusable ones. It’s only rocket science.”

• Uber/Lyft/DiDi: “Taxis & buses. You’ve invented taxis & buses. And rental bikes.”

• Instacart/Ocado/Uber Eats: “We’ll do Kozmo.com/Webvan again, minus the bankruptcy.”

• PayPal: “Everyone else’s online payments has failed, so we’ll do it again, with anonymous cryptography! On phones! In 1998_28ya! End-users love cryptography, right? If the software doesn’t work out, I guess we’ll… do something else. We’re not sure what.” Later: “oh, apparently eBay sellers like us so much they’re making their own promotional materials? Huh. What if… instead of ‘threatening to sue them’, we tried ‘working with them’?”

• Venmo: “TextPayMe worked out well, right?”

• Patreon: “Online micropayments & patronage schemes have failed hundreds of times and became a ’90s punchline; might as well try again.”

• Bitcoin: “Every online-only currency from DigiCash to Flooz.com to e-gold to [too many to list] has either failed or been shut down by governments; so, we’ll use ‘proof of work’—it’s a hilariously expensive cryptographic thing we just made up which has zero theoretical support for actually ensuring decentralization & censorproofing, and was roundly mocked by almost every e-currency enthusiast who bothered to read the whitepaper.”

• Seamless/Grubhub/Uber Eats/DoorDash/Slice (!): “CyberSlice blew through $201.02^$100₂₀₀₀m+ trying to sell pizza online, but this time will be different.”

• FedEx: “The experienced & well-capitalized Emery Air Freight is already trying and failing to make the hub-and-spoke air delivery method work; I’ll blow my inheritance on trying to compete with them while being so undercapitalized I’ll have to commit multiple crimes to keep FedEx afloat like literally gambling the company’s money at Las Vegas.”

• Lotus 1-2-3: “VisiCalc literally invented the spreadsheet, has owned the market for 4 years despite clones like Microsoft’s, and singlehandedly made the Apple II PC a mega-success; we’ll write our own spreadsheet from scratch, fixing some of VisiCalc’s problems, and beat them to the IBM PC. Everyone will buy it simply because it’ll be slightly better.”

• Airbnb: “We’ll max out our credit cards to let people illegally rent out their air mattresses en route to eating the hotel industry. VCs will literally escape through the bathroom to avoid talking to us.”

• Stripe: “Banks & online payment processors like PayPal are heavily-regulated inefficient monopolies which really suck; we’ll make friends with some banks and run a payment processor which doesn’t suck. Our signature selling point will be that it takes fewer lines of code to set up, so programmers will like us.”

• LinkedIn: “We’ll do social networking like has been already patented by SixDegrees.com, forcing us to buy their patent.”

• Slack: “IRC+email but infinitely slower & more locked in. Businesses won’t be able to get enough of it; employees will love to hate it.”

• English Wikipedia: “We’ll compete with Microsoft Encarta, the Encyclopedia Britannica, H2G2, Everything2, Interpedia, The Distributed Encyclopedia Project (TDEP), TheInfo, & GNU’s GNE by letting literally anyone edit some draft articles for Nupedia.”

• Zoom: “Skype has a literally 15-year headstart, but we can do so much better, and maybe something will make everyone suddenly want to video-conference after all this time avoiding it as much as possible?”

• “QR code”? Dude, don’t you remember CueCat at all?

You don’t have to be bipolar to be an entrepreneur, but it might help. (“The most successful people I know believe in themselves almost to the point of delusion…”)

Why so many failed predecessors?

Part of the explanation is survivorship bias causing hindsight bias. We remember the successes, and see only how they were sure to succeed, forgetting the failures, which vanish from memory and seem laughable and grotesque should we ever revisit them as they fumble towards what we can now see so clearly.

The origins of many startups are highly idiosyncratic & chancy; eg. why should a podcasting company, Odeo, have led to Twitter? Survival alone is highly chancy, and founders can often see times where it came down to a dice roll. Like historical events in general (Risi et al 2019), the importance of an event or change is often known only in retrospect. Overall, the odds of success are low, and the rewards are not great for most—despite the skewed distribution producing occasional eye-popping returns in a few cases, the risk-adjusted return of the technology sector or VC funds is not that much greater than the broader economy.

“Of course Google was always going to be a huge success because of PageRank and also (post hoc theorizing) Z, Y, & Z”, except for the minor problem that Google was merely one of many search engines, great perhaps but not profitable, and didn’t hit upon a profitable business model—much less a unicorn-worth model—until 4 years later when it copied Overture’s advertising auction, which was its salvation (In The Plex); in the mean time, Google had to sign potentially fatal deals or risking burning through the last of its capital when minor technical glitches derailed vital deals. (All of which was doubtless why Page & Brin tried & failed to sell Google to AltaVista & Excite & Yahoo early on, and negotiated a possible sale with Yahoo as late as 2002_24ya which they ultimately rejected.) In a counterfactual world, Google went down in flames quite easily because it never hit upon the advertising innovations that saved it, no matter how much you liked PageRank, and anything else is hindsight bias. Fedex, early on, couldn’t make payroll and the founder famously kept the planes flying only by gambling the last of their money in Las Vegas, among other near-death experiences & crimes—just one of many startups doing highly questionable things. Both SpaceX & Tesla have come within days (or hours) of bankruptcy, in 2008_18ya and 2013_13ya; in the former case, Musk borrowed money from friends to pay his rent after 3 rocket failures in a row, and in the latter, Musk reportedly went as far as securing a pledge from Google to buy Tesla outright rather than let it go bankrupt (Vance2015). Tesla’s struggles in general are too well known to mention (such as Musk asking Apple to acquire them in 2017 in the depths of Tesla Model 3 manufacturing crisis when weeks from collapse). Mark Zuckerberg, in 2004_22ya, wanted nothing more than to sell Facebook for a few million dollars so he could work on his P2P filesharing program, Wirehog, commenting that the sale price just needed to be large enough “to propel Wirehog.” Youtube was a dating site. Stewart Butterfield wanted to make a MMORPG game which failed, and all he could salvage out of it was the photo-sharing part, which became Flickr; he still really wanted to make a MMORPG, so after Flickr, he founded a company to make the MMORPG Glitch which… also failed, so after trying to shut down his company and being told not to by his investors, he salvaged the chat part from it, which became Slack. And, consistent with the idea that there is a large ineradicable element of chance to it, surveys of startups suggest that while there are individual differences in odds of success (‘skill’), any founder learning curve (‘learning-by-doing’) is small & success probability remains low regardless of experience (Gompers2010, Parker2011, Gottschalk2014), and experienced entrepreneurs still have low odds of forecasting startups achieving commercialization at all, approaching random predictions in “non-R&D-intensive sectors” (eg. Scott et al 2019, McKenzie & Sansone2019).

Thiel (Zero to One; original): “Every moment in business happens only once. The next Bill Gates will not build an operating system. The next Larry Page or Sergey Brin won’t make a search engine. And the next Mark Zuckerberg won’t create a social network. If you are copying these guys, you aren’t learning from them.”. This is true but I would say it reverses the order (‘N to N+1’?): you will not be the next Bill Gates, because Bill Gates was not the first and only Bill Gates, he was, pace Stigler’s Law, the last Bill Gates; many people made huge fortunes off OSes, both before and after Gates—you may have forgotten Wang, but hopefully you remember Steve Jobs (before, Mac) and Steve Jobs (after, NeXT). Similarly, Mark Zuckerberg was not the first and only Zuckerberg, he was the last Zuckerberg; many people made social networking fortunes before him—maybe Orkut didn’t make its Google inventor a fortune, but you can bet that MySpace’s DeWolfe and Anderson did well. And there were plenty of lucrative search engine founders (is still a billionaire? Yes).

Gates, however, proved the market, and refined the Gates strategy to perfection, using up the trick; no one can get historically rich off shipping an OS plus some business productivity software because there are too many competitors and too many players interested in ensuring that no one becomes the next Gates, and so opportunity has moved on to the next area.

A successful company rewrites history and its precursors: history must be lived forward, progressing to an obscured destination; but we always recall it backwards, progressing towards the clarity of the present.

Can you ask researchers if the time is ripe? Well: researchers have a slight conflict of interest in the matter, and are happy to spend arbitrary amounts of money on topics without anything to show for it. After all, why would they say no?

Scott Fisher:

I ended up doing more work in Japan than anything else because Japan in general is so tech-smitten and obsessed that they just love it [VR]. The Japanese government in general was funding research, building huge research complexes just to focus on this. There were huge initiatives while there was nothing happening in the US. I ended up moving to Japan and working there for many years.

Indeed, this would have around the Japanese boondoggle the Fifth Generation Project (note that despite Japan’s reputed prowess at robotics, it is not Japan’s robots who went into Fukushima / flying around the Middle East / revolutionizing agriculture and construction). All those ‘huge initiatives’ and…? Don’t ask Fisher, he’s hardly going to say, “oh yeah, all the money was completely wasted, we were trying to do it too soon; our bad”. And Lanier implies that Japan alone spent a lot of money:

Jaron Lanier: “The components have finally gotten cheap enough that we can start to talk about them as being accessible in the way that everybody’s always wanted…Moore’s law is so interesting because it’s not just the same components getting cheaper, but it really changes the way you do things. For instance, in the old days, in order to tell where your head was so that you could position virtual content to be standing still relative to you, we used to have to use some kind of external reference point, which might be magnetic, ultrasonic, or optical. These days you put some kind of camera on the head and look around in the room and it just calculates where you are—the headsets are self-sufficient instead of relying on an external reference infrastructure. That was inconceivable before because it would have been just so expensive to do that calculation. Moore’s law really just changes again and again, it re-factors your options in really subtle and interesting ways.”

Kevin Kelly: “Our sense of history in this world is very dim and very short. We were talking about the past: VR wasn’t talked about for a long time, right? 35 years. Most people have no idea that this is 35 years old. 30 years later, it’s the same headlines. Was the technological power just not sufficient 30 years ago?”

…[On the Nintendo Power Glove, based on a VPL dataglove design:]

JL: “Both I and a lot of other people really, really wanted to get a consumerable version of this stuff out. We managed to get a taste of the experience with something called the Power Glove…Sony actually brought out a little near-eye display called Virtual Boy; not very good, but they gave it their best shot. and there were huge projects that have never been shown to the public to try to make a consumable [VR product], very expensive ones. Counting for inflation, probably more money was spent [than] than Facebook just spent on Oculus. We just could never, never, never get it quite there.”

KK: “Because?”

JL: “The component cost. It’s Moore’s law. Sensors, displays… batteries! Batteries is a big one.”

Issues like component cost were not something that could be solved by a VR research project, no matter how ambitious. Those were hard binding limits, and to solve them by creating tiny high-resolution LED/LCD screens for smartphones, required the benefit of decades of Moore’s law and the experience curve effects of manufacturing billions of smartphones.

Researchers in general have no incentive to say, “this is not the right time, wait another 20 years for Moore’s law to make it doable”, even if everyone in the field is perfectly aware of this—Palmer Luckey:

I spent a huge amount of time reading…I think that there were a lot of people that were giving VR too much credit, because they were working as VR researchers. You don’t want to publish a paper that says, ‘After the study, we came to the conclusion that VR is useless right now and that we should just not have a job for 20 years.’ There were a few people that basically came to that conclusion. They said, ‘Current VR gear is low field of view, high lag, too expensive, too heavy, can’t be driven properly from consumer-grade computers, or even professional-grade computers.’ It turned out that I wasn’t the first person to realize these problems. They’d been known for decades.

AI researcher Donald Michie, claimed in 1970_56ya, based on a 1969_57ya poll, that a majority of AI researchers estimated 10–100 years for AGI (or 1979^–₉₀2069) and that “There is also fair agreement that the chief obstacles are not hardware limitations.” While AI researcher surveys still suggest that wasn’t a bad range (Gruetzemacher et al 2019), the success of deep learning makes clear that hardware was a huge limitation, and resources 50 years ago fell short by at least 6 orders of magnitude. Michie went on to point out that in a previous case, Charles Babbage, his work was foredoomed by it being an “unripe time” due to hardware limitations and represented a complete waste of time & money. This, arguably, was the case for Michie’s own research.

So you don’t know the timing well enough to reliably launch. You can’t imitate a successful entrepreneur, the time is past. You can’t foresee what will be successful based on what has been successful; you can’t even foresee what won’t be successful based on what was already unsuccessful; and you can’t ask researchers because they are incentivized to not know the timing any better than anyone else.

Can you at least profit from your knowledge of the outcome? Here again we must be pessimistic.

Certainty is irrelevant, you still have problems making use of this knowledge. Example: in retrospect, we know everyone wanted computers, OSes, social networks—but the history of them is strewn with flaming rubble. Suppose you somehow knew in 2000_26ya that “in 2010, the founder of the most successful social network will be worth at least $10b”; this is a falsifiable belief at odds with all conventional wisdom and about a tech that blindsided everyone. Yet, how useful would this knowledge be, really? What would you do with it? Do you have the capital to start a VC fund of your own, and throw multi-million-dollar investments at every social media until finally in 2010_16ya you knew for sure that Facebook was the winning ticket and could cash out in the IPO? I doubt it.

It’s difficult to invest in ‘computers’ or ‘AI’ or ‘social networking’ or ‘VR’; there is no index for these things, and it is hard to see how there even could be such a thing. (How do you force all relevant companies to sell tradable stakes? “If people don’t want to go to the ball game, how are you going to stop them?” as Yogi Berra asked.) There is no convenient CMPTR you can buy 100 shares of and hold indefinitely to capture gains from your optimism about computers. IBM and Apple both went nearly bankrupt at points, and Microsoft’s stock has been flat since 1999_27ya or whenever (translating to huge real losses and opportunity costs to long-term holders of it); Cisco, the darling of the dot-com bubble—“sell shovels during a gold rush”—was one of the best-performing stocks ever up to its all-time high in 2000_26ya. If you knew for certain that Facebook would be as huge as it was, what stocks, exactly, could you have invested in, pre-IPO, to capture gains from its growth? Remember, you don’t know anything else about the tech landscape in the 2000s, like that Google will go way up from its IPO, you don’t know about Apple’s revival under Jobs—all you know is that a social network will exist and will grow hugely. Why would anyone think that the future of smartphones would be won by “a has-been 1980s PC maker and an obscure search engine”? (The best I can think of would be to sell any Murdoch stock you owned when you heard they were buying MySpace, but offhand I’m not sure that Murdoch didn’t just stagnate rather than drop as MySpace increasingly turned out to be a writeoff.) In the hypothetical that you didn’t know the name of the company, you might’ve bought up a bunch of Google stock hoping that Orkut would be the winner, but while that would’ve been a decent investment (yay!) it would have had nothing to do with Orkut (oops)…

And even when there are stocks available to buy, you only benefit based on the specifics—like one of the existing stocks being a winner, rather than all the stocks being eaten by some new startup. Let’s imagine a different scenario, where instead you were confident that home robotics were about to experience a huge growth spurt. Is this even nonpublic knowledge at all? The world economy grows at something like 2% a year, labor costs generally seem to go up, prices of computers and robotics usually falls… Do industry projections expect to grow their sales by <25% a year?

But say that the market is wrongly pessimistic. If so, you might spend some of your hypothetical money on whatever the best approximation to a robotics index fund you can find, as the best of a bunch of bad choices. (Checking a few random entries in Wikipedia, as of 2012_14ya, maybe a fifth of the companies are publicly traded, and the private ones include the ones you might’ve heard of like Boston Robotics or Kiva so… that will be a small unrepresentative index.) Suppose the home robotic growth were concentrated in a single private company which exploded into the billions of annual revenue and took away the market share of all the others, forcing them to go bankrupt or merge or shrink. Home robotics will have increased just as you believed—keikaku doori!—yet your ‘index fund’ gone bankrupt (reindex when one of the robotics companies collapses? Reindex into what, another doomed firm?). Then after your special knowledge has become public knowledge, the robotics company goes public, and by EMH, their shares become a normal investment.

Morgan Housel:

There were 272 automobile companies in 1909_117ya. Through consolidation and failure, 3 emerged on top, 2 of which went bankrupt. Spotting a promising trend and a winning investment are two different things.

Is this impossibly rare? It sounds like Facebook! They grew fast, roflstomped other social networks, stayed private, and post-IPO, public investors have not profited all that much compared to even late investors.

Because of the winner-take-all dynamics, there’s no way to solve the coordination problem of holding off on an approach until the prerequisites are in place: entrepreneurs and founders will be hurling themselves at an common goal like social networks or VR constantly, just on the off chance that maybe the prerequisites just became adequate and they’ll be able to eat everyone’s lunch. A predictable waste of money, perhaps, but that’s how the incentives work out. It’s a weird perspective to take, but we can think of other technologies which may be like this.

Bitcoin is a topical example: it’s still in the early stages where it looks either like a genius stroke to invest in, or a fool’s paradise/Ponzi scheme. In my first draft of this essay in 2012, I noted that we see what looks like a Bitcoin bubble as the price inflates from ~$0 to $198.07^$130₂₀₁₂—yet, if Bitcoin were the Real Deal, we would expect large price increases as people learn of it and it directly gains value from increased use, an ecosystem slowly unlocking the fancy cryptographic features, etc. And in 2019, with 2012_14ya a distant memory, well, one could say something similar, just with larger numbers…

Or take niche visionary technologies: if cryonics was correct in principal, yet turned out to be worthless for everyone doing it before 2030 (because the wrong perfusion techniques or cryopreservatives were used and some critical bit of biology was not vitrified) while practical post-2030 say, it would simply be yet another technology where visionaries were ultimately right despite all nay-saying and skepticism from normals but nevertheless wrong in a practical sense because they jumped on it too early, and so they wasted their money.

Indeed, do many things come to pass.

Where does this leave us? In what I would call, in a nod to Thiel’s ‘definite’ vs ‘indefinite optimism’, definitely-maybe optimism. Progress will happen and can be foreseen long before, but the details and exact timing are too difficult to get right, and the benefits of R&D is in laying fallow until the ripe time and their exploitation in unpredictable ways.

Returning to Donald Michie: one could make fun of his extremely overly-optimistic AI projections, and write him off as the stock figure of the biased AI researcher blinded by the ‘Maes-Garreau law’ where AI is always scheduled for right when a researcher will retire but while he was wrong, it is unclear this was a mistake because in other cases, an apparently doomed research project—Marconi’s attempt to radio across the Atlantic ocean—succeeded because of an ‘unknown unknown’—the Kennelly-Heaviside layer. We couldn’t know for sure that such projections were wrong, and the amount of money being spent back then on AI was truly trivial (and the commercial spinoffs likely paid for it all anyway).

Further, on the gripping hand, Michie suggests that such research efforts like Babbage’s should be thought of not as commercial R&D, expected to usually pay off right now, but as prototypes buying optionality, demonstrating that a particular technology was approaching its ‘ripe time’ & indicating what are the bottlenecks, so society can go after the bottlenecks and then has the option to scale up the prototype as soon as the bottlenecks are fixed. Richard Hamming describes the ripe time as when new ideas or methods finally enable attacks on consequential problems (ie. high Value of Information). Edward Boyden describes the development of both optogenetics & expansion microscopy as “failure rebooting”, revisiting (failed) past ideas which may now be workable in the light of progress in other areas. As time passes, the number of options may open up, and any of them may bypass what was formerly a necessary or serial dependency which was fatal. Enough progress in one domain (particularly computing power), can sometimes make up for stasis in another domain.

So, what Babbage should have aimed for is not making a practical thinking machine which could churn out naval tables, but demonstrating that a programmable thinking machine is possible & useful, and currently limited by the slowness & size of its mechanical logic—so that transistors could be pursued with higher priority by governments, and programmable computers could be created with transistors as soon as possible, instead of the historical course of a meandering piecemeal development where Babbage’s work was forgotten & then repeatedly reinvented with delays (eg. Konrad Zuse vs von Neumann). Similarly, the benefit of taking Moore’s law seriously is that one can plan ahead to take advantage of it even if one doesn’t know exactly when, if ever, it will happen.

Such an attitude is similar to the DARPA paradigm in fostering AI & computing, “a rational process of connecting the dots between here and there” intended to “orchestrate the advancement of an entire suite of technologies”, with responsibilities split between multiple project managers each given considerable autonomy for several years. These project managers tend to pick polarizing projects rather than consistent projects (Goldstein & Kearney2017), ones which generate disagreement among reviews or critics. Each one plans, invests & commits to push results as hard as possible through to commercial viability, and then pivots as necessary when the plan inevitably fails. (DARPA indeed saw itself as much like a VC firm.)

The benefit for someone like DARPA of a forecast like Moore’s law is that it provides one fixed trend to gauge overall timing to within a decade or so, and look for those dots which have lagged behind and become reverse salients. For an entrepreneur, the advantage of exponential thinking is more fatalistic: being able to launch in the window of time between just after technical feasibility but before someone else randomly gives it a try; if wrong and it was always impossible, it doesn’t matter when one launches, and if wrong because timing is wrong, one’s choice is effectively random and little is lost by delay.

This presents a conflict between personal and social incentives. Socially, one wants people regularly tossing their bodies into the marketplace to be trampled by uncaring forces just on the off chance that this time it’ll finally work, and since the critical factors are unknown and constantly changing, one needs a sacrificial startup every once in a while to check (for a good idea, no amount of failures is enough to prove that it should never be tried—many failures just implies that there should be a backoff). Privately, given the skewed returns, diminishing utility, the oversized negative impacts (a bad startup can ruin one’s life and drive one to suicide), the limited number of startups any individual can engage in (yielding gambler’s ruin), and the fact that startups & VC will capture only a minute percentage of the total gains from any success (most of which will turn into consumer surplus/positive externalities), the only startups that make any rational sense, which you wouldn’t have to be crazy to try, are the overdetermined ones which anyone can see are a great idea. However, those are precisely the startups that crazy people will have done years before when they looked like bad ideas, avoiding the waste of delay. Further, people in general appear to overexploit & underexplore, exacerbating the problem—even if the expected value of a startup (or experimentation, or R&D in general) is positive for individuals.

So, it seems that rapid progress depends on crazy people.

There is a more than superficial analogy here, I think, to Thompson sampling/posterior sampling (PSRL) Bayesian reinforcement learning. In RL’s multi-armed bandit setting, each turn one has a set of ‘arms’ or options with unknown payoffs and one wants to maximize the total long-term reward. The difficulty is in coping with failure: even good options may fail many times in a row, and bad options may succeed, so options cannot simply be ruled out after a failure or two, and if one is too hasty to write an option off, one may take a long time to realize that, losing out for many turns.

One of the simplest & most efficient MAB solutions, which maximizes the total long-term reward and minimizes ‘regret’ (opportunity cost), is Thompson sampling & its generalization PSRL: randomly select each option with a probability equal to the current estimated probability that it is the most profitable option. This explores all options initially but gradually homes in on the most profitable option to exploit most of the time, while still occasionally exploring all the other options once in a while, just in case; strictly speaking Thompson sampling will never ban an option permanently, the probability of selecting an option merely becomes vanishingly rare. Bandit settings can further assume that options are ‘restless’ and the optimal option may ‘drift’ over time or ‘run out’ or ‘switch’, in which case one also estimates the probability that an option has switched, and when it does, one changes over to the new best option; instead of the regular Thompson sampling where bad options become ever more unlikely to be tried, a restless bandit results in constant low-level exploration because one must constantly check lest one fails to notice a switch.

This bears a resemblance to startup rates over time: an initial burst of enthusiasm for a new ‘option’, when it still has high prior probability of being the most profitable option at the moment, triggers a bunch of startups selecting that option, but then when they fail, the posterior probability drops substantially; however, even if something now looks like a bad idea, there will still be people every once in a while who insist on trying again anyway, and, because the probability is not 0, once in a while they succeed wildly and everyone is astonished that ‘so, X is a thing now!’

In DARPA’s research funding and VC, they often aren’t looking for a plan which looks good on average to everyone, or which no one can find any particular problem with, but something closer to a plan which at least one person thinks could be awesome for some reason. An additional analogy from reinforcement learning is PSRL, which handles more complex problems by committing to a strategy and following it until the end and either success/failure. A naive Thompson sampling would do badly in a long-term problem because at every step, it would ‘change its mind’ and be unable to follow any plan consistently for long enough to see what happens; what is necessary is to do ‘deep exploration’, following a single plan long enough to see how it works, even if one thinks that plan is almost certainly wrong, one must “Disagree and commit”. The average of multiple plans is often worse than any single plan. The most informative plan is the most polarizing one.

The system as a whole can be seen in RL terms. One theme I notice in many systems is that they follow a multi-level optimization structure where slow blackbox methods give rise to more efficient Bayesian inference. Ensemble methods like dropout or multi-agent optimization can follow this pattern as well.

A particularly germane example here is Krafft et al 2016/Krafft2017 (discussion), which examines a large dataset of trades made by eToro online traders, who are able to clone financial trading strategies of more successful traders; as traders find successful strategies, others gradually imitate them, and so the system as a whole converges on better strategies in what they identify as a sort of particle filter-like implementation of “distributed Thompson sampling” which they dub “social sampling”. So for the most part, traders clone popular strategies, but with certain probabilities, they’ll randomly explore rarer apparently-unsuccessful strategies.

This sounds a good deal like individuals pursuing standard careers & occasionally exploring unusual strategies like a startup; they will occasionally explore strategies which have performed badly (ie. previous similar startups failed). Entrepreneurs, with their speculations and optimistic biases, serve as randomization devices to sample a strategy regardless of the ‘conventional wisdom’, which at that point may be no more than an information cascade; information cascades, however, can be broken by the existence of outliers who are either informed or act at random (“misfits”). While each time a failed option is tried, it may seem irrational (“how many times must VR fail before people finally give up on it‽”), it was still rational in the big picture to give it a try, as this collective strategy collectively minimizes regret & maximizes collective total long-term returns—as long as failed options aren’t tried too often.

What does this analogy suggest? The two failure modes of a MAB algorithm are investing too much in one option early on, and then investing too little later on; in the former, you inefficiently buy too much information on an option which happened to have good luck but is not guaranteed to be the best at the expense of others (which may in fact be the best), while in the latter, you buy too little & risk permanently making a mistake by prematurely rejecting an apparently-bad option (which simply had bad luck early on). To the extent that VC/startups stampede into particular sectors, this leads to inefficiency of the first time—were so many ‘green energy’ startups necessary? When they began failing in a cluster, information-wise, that was highly redundant. And then on the other hand, if a startup idea becomes ‘debunked’, and no one is willing to invest in it ever, that idea may be starved of investment long past its ripe time, and this means big regret.

I think most people are aware of fads/stampedes in investing, but the latter error is not so commonly discussed. One idea is that a VC firm could explicitly track ideas that seem great but have had several failed startups, and try to schedule additional investments at ever greater intervals (similar to DS-PRL), which bounds losses (if the idea turns out to be truly a bad idea after all) but ensures eventual success (if a good one). For example, even if online pizza delivery has failed every time it’s tried, it still seems like a good idea that people will want to order pizza online via their smartphones, so one could try to do a pizza startup 2.5 years later, then 5 years later, then 10 years, then 20 years, or perhaps every time computer costs drop an order of magnitude, or perhaps every time the relevant market doubles in size? Since someone wanting to try the business again might not pop up at the exact time desired, a VC might need to create one themselves by trying to inspire someone to do it.

What other lessons could we draw if we thought about technology this way? The use of lottery grants is one idea which has been proposed, to help break the over-exploitation fostered by peer review; the randomization gives disfavored low-probability proposals (and people) a chance. If we think about multi-level optimization systems & population-based training, and optimization of evolution like strong amplifiers (which resemble small but networked communities: Pavlogiannis et al 2018), that would suggest we should have a bias against both large and small groups/institutes/granters, because small ones are buffeted by random noise/drift and can’t afford well-powered experiments, but large ones are too narrow-minded. But a network of medium ones can both explore well and then efficiently replicate the best findings across the network to exploit them.