Oct 10, 2018
Ben Pace and I (Richard Ngo) recently did a public double crux at the Berkeley REACH on how valuable it is for people to go into AI policy and strategy work: I was optimistic and Ben was pessimistic. During the actual event, we didn't come anywhere near to finding a double crux on that issue. But after a lot of subsequent discussion, we've come up with some more general cruxes about where impact comes from.
I found Ben's model of how to have impact very interesting, and so in this post I've tried to explain it, along with my disagreements. Ben liked the goal of writing up a rough summary of our positions and having further discussion in the comments, so while he edited it somewhat he doesn’t at all think that it’s a perfect argument, and it’s not what he’d write if he spent 10 hours on it. He endorsed the wording of the cruxes as broadly accurate.
(During the double crux, we also discussed how the heavy-tailed worldview applies to community building, but decided on this post to focus on the object level of what impact looks like.)
Note from Ben: “I am not an expert in policy, and have not put more than about 20-30 hours of thought into it total as a career path. But, as I recently heard Robin Hanson say, there’s a common situation that looks like this: some people have a shiny idea that they think about a great deal and work through the details of, that folks in other areas are skeptical of given their particular models of how the world works. Even though the skeptics have less detail, it can be useful to publicly say precisely why they’re skeptical.
In this case I’m often skeptical when folks tell me they’re working to reduce x-risk by focusing on policy. Folks doing policy work in AI might be right, and I might be wrong, but it seemed like a good use of time to start a discussion with Richard about how I was thinking about it and what would change my mind. If the following discussion causes me to change my mind on this question, I’ll be really super happy with it.”
A heavy-tailed distribution is one where the probability of extreme outcomes doesn’t drop very rapidly, meaning that outliers therefore dominate the expectation of the distribution. Owen Cotton-Barratt has written a brief explanation of the idea here. Examples of heavy-tailed distributions include the Pareto distribution and the log-normal distribution; other phrases people use to point at this concept include ‘power laws’ (see Zero to One) and ‘black swans’ (see the recent SSC book review). Wealth is a heavy-tailed distribution, because many people are clustered relatively near the median, but the wealthiest people are millions of times further away. Human height and weight and running speed are not heavy-tailed; there is no man as tall as 100 people.
There are three key claims that make up Ben's view.
The first claim is that, since the industrial revolution, we live in a world where the impact that small groups can have is much more heavy-tailed than in the past.
The second claim is that you should put significant effort into re-orienting yourself to use high-variance strategies.
The third claim is that AI policy is not a good place to get big wins nor to learn the relevant mindset.
The above is not a full, gears-level analysis of how to find and exploit a heavy tail, because almost all of the work here lies in identifying the particular strategy. Nevertheless, because of the considerations above, Ben thinks that talented, agenty and rational people should be able in many cases to identify places to win, and then execute those plans, and that this is much less the case in policy.
I disagree with Ben on all three points above, to varying degrees.
On the first point, I agree that the distribution of success has become much more heavy-tailed since the industrial revolution. However, I think the distribution of success is often very different from the distribution of impact, because of replacement effects. If Facebook hadn't become the leading social network, then MySpace would have. If not Google, then Yahoo. If not Newton, then Leibniz (and if Newton, then Leibniz anyway). Probably the alternatives would have been somewhat worse, but not significantly so (and if they were, different competitors would have come along). The distinguishing trait of modernity is that even a small difference in quality can lead to a huge difference in earnings, via network effects and global markets. But that isn't particularly interesting from an x-risk perspective, because money isn't anywhere near being our main bottleneck.
You might think that since Facebook has billions of users, their executives are a small group with a huge amount of power, but I claim that they're much more constrained by competitive pressures than they seem. Their success depends on the loyalty of their users, but the bigger they are, the easier it is for them to seem untrustworthy. They also need to be particularly careful since antitrust cases have busted the dominance of several massive tech companies before. (While they could swing a few elections before being heavily punished, I don’t think this is unique to the internet age - a small cabal of newspaper owners could probably have done the same centuries ago). Similarly, I think the founders of Wikipedia actually had fairly little counterfactual impact, and currently have fairly little power, because they're reliant on editors who are committed to impartiality.
What we should be more interested in is cases where small groups didn't just ride a trend, but actually created or significantly boosted it. Even in those cases, though, there's a big difference between success and impact. Lots of people have become very rich from shuffling around financial products or ad space in novel ways. But if we look at the last fifty years overall, they're far from dominated by extreme transformative events - in fact, Western societies have changed very little in most ways. Apart from IT, our technology remains roughly the same, our physical surroundings are pretty similar, and our standards of living have stayed flat or even dropped slightly. (This is a version of Tyler Cowen and Peter Thiel's views; for a better articulation, I recommend The Great Stagnation or The Complacent Class). Well, isn't IT enough to make up for that? I think it will be eventually, as AI develops, but right now most of the time spent on the internet is wasted. I don't think current IT has had much of an effect by standard metrics of labour productivity, for example.
Should you pivot?
Ben might claim that this is because few people have been optimising hard for positive impact using high-variance strategies. While I agree to some extent, I also think that there are pretty strong incentives to have impact regardless. We're in the sort of startup economy where scale comes first and monetisation comes second, and so entrepreneurs already strive to create products which influence millions of people even when there’s no clear way to profit from them. And entrepreneurs are definitely no strangers to high-variance strategies, so I expect most approaches to large-scale influence to already have been tried.
On the other hand, I do think that reducing existential risk is an area where a small group of people are managing to have a large influence, a claim which seems to contrast with the assertion above. I’m not entirely sure how to resolve this tension, but I’ve been thinking lately about an analogy from finance. Here's Tyler Cowen:
I see a lot of money managers, so there’s Ray Dalio at Bridgewater. He saw one basic point about real interest rates, made billions off of that over a great run. Now it’s not obvious he and his team knew any better than anyone else.
Peter Lynch, he had fantastic insights into consumer products. Use stuff, see how you like it, buy that stock. He believed that in an age when consumer product stocks were taking off.
Warren Buffett, a certain kind of value investing. Worked great for a while, no big success, a lot of big failures in recent times.
The analogy isn’t perfect, but the idea I want to extract is something like: once you’ve identified a winning strategy or idea, you can achieve great things by exploiting it - but this shouldn’t be taken as strong evidence that you can do exceptional things in general. For example, having a certain type of personality and being a fan of science fiction is very useful in identifying x-risk as a priority, but not very useful in founding a successful startup. Similarly, being a philosopher is very useful in identifying that helping the global poor is morally important, but not very useful in figuring out how to solve systemic poverty.
From this mindset, instead of looking for big wins like “improving intellectual coordination”, we should be looking for things which are easy conditional on existential risk actually being important, and conditional on the particular skillsets of x-risk reduction advocates. Another way of thinking about this is as a distinction between high-impact goals and high-variance strategies: once you’ve identified a high-impact goal, you can pursue it without using high-variance strategies. Startup X may have a crazy new business idea, but they probably shouldn't execute it in crazy new ways. Actually, their best bet is likely to be joining Y Combinator, getting a bunch of VC funding, and following Paul Graham's standard advice. Similarly, reducing x-risk is a crazy new idea for how to improve the world, but it's pretty plausible that we should pursue it in ways similar to those which other successful movements used. Here are some standard things that have historically been very helpful for changing the world:
My prior says that all of these things matter, and that most big wins will be due to direct effects on these things. The last two are the ones which we’re disproportionately lacking; I’m more optimistic about the latter for a variety of reasons.
AI policy is a particularly good place to have a large impact.
Here's a general argument: governments are very big levers, because of their scale and ability to apply coercion. A new law can be a black swan all by itself. When I think of really massive wins over the past half-century, I think about the eradication of smallpox and polio, the development of space technology, and the development of the internet. All of these relied on and were driven by governments. Then, of course, there are the massive declines in poverty across Asia in particular. It's difficult to assign credit for this, since it's so tied up with globalisation, but to the extent that any small group was responsible, it was Asian governments and the policies of Deng Xiaoping, Lee Kuan Yew, Rajiv Gandhi, etc.
You might agree that governments do important things, but think that influencing them is very difficult. Firstly, that's true for most black swans, so I don't think that should make policy work much less promising even from Ben's perspective. But secondly, from the outside view, our chances are pretty good. We're a movement comprising many very competent, clever and committed people. We've got the sort of backing that makes policymakers take people seriously: we're affiliated with leading universities, tech companies, and public figures. It's likely that a number of EAs at the best universities already have friends who will end up in top government positions. We have enough money to do extensive lobbying, if that's judged a good idea. Also, we're correct, which usually helps. The main advantage we're missing is widespread popular support, but I don't model this as being crucial for issues where what's needed is targeted interventions which "pull the rope sideways". (We're also missing knowledge about what those interventions should be, but that makes policy research even more valuable).
Here's a more specific route to impact: in a few decades (assuming long timelines and slow takeoff) AIs that are less generally intelligent that humans will be causing political and economic shockwaves, whether that's via mass unemployment, enabling large-scale security breaches, designing more destructive weapons, psychological manipulation, or something even less predictable. At this point, governments will panic and AI policy advisors will have real influence. If competent and aligned people were the obvious choice for those positions, that'd be fantastic. If those people had spent several decades researching what interventions would be most valuable, that'd be even better.
This perspective is inspired by Milton Friedman, who argued that the way to create large-scale change is by nurturing ideas which will be seized upon in a crisis.
Only a crisis - actual or perceived - produces real change. When that crisis occurs, the actions that are taken depend on the ideas that are lying around. That, I believe, is our basic function: to develop alternatives to existing policies, to keep them alive and available until the politically impossible becomes the possible.
The major influence of the Institute of Economic Affairs on Thatcher’s policies is an example of this strategy’s success. An advantage of this approach is that it can be implemented by clusterings of like-minded people collaborating with each other; for that reason, I'm not so worried about policy work cultivating the wrong mindset (I'd be more worried on this front if policy researchers were very widely spread out).
Another fairly specific route to impact: several major AI research labs would likely act on suggestions for coordinating to make AI safer, if we had any. Right now I don’t think we do, and so research into that could have a big multiplier. If a government ends up running a major AI lab (which seems pretty likely conditional on long timelines) then they may also end up following this advice, via the effect described in the paragraph above.
Underlying generators of this disagreement
More generally, Ben and I disagree on where the bottleneck to AI safety is. I think that finding a technical solution is probable, but that most solutions would still require careful oversight, which may or may not happen (maybe 50-50). Ben thinks that finding a technical solution is improbable, but that if it's found it'll probably be implemented well. I also have more credence on long timelines and slow takeoffs than he does. I think that these disagreements affect our views on the importance of influencing governments in particular.
We also have differing views on what the x-risk reduction community should look like. I favour a broader, more diverse community; Ben favours a narrower, more committed community. I don't want to discuss this extensively here, but I will point out that there are many people who are much better at working within a system than outside it - people who would do well in AI safety PhDs, but couldn't just teach themselves to do good research from scratch like Nate Soares did; brilliant yet absent-minded mathematicians; people who could run an excellent policy research group but not an excellent startup. I think it's valuable for such people (amongst which I include myself), to have a "default" path to impact, even at the cost of reducing the pressure to be entrepreneurial or agenty. I think this is pretty undeniable when it comes to technical research, and cross-applies straightforwardly to policy research and advocacy.
Ben and I agree that going into policy is much more valuable if you're thinking very strategically and out of the "out of the box" box than if you're not. Given this mindset, there will probably turn out to be valuable non-standard things which you can do.
Do note that this essay is intrinsically skewed since I haven't portrayed Ben's arguments in full fidelity and have spent many more words arguing my side. Also note that, despite being skeptical about some of Ben's points, I think his overall view is important and interesting and more people should be thinking along similar lines.
Thanks to Anjali Gopal for comments on drafts.