I agree that Luke here overstates the significance of my result, but I do think you miss the point a bit or are uncharitable. Regardless of whether making predictions about your own behavior is fundamentally difficult, we don't yet understand any formal framework that can capture reasoning of the form “my decisions are good because my beliefs correspond to reality.” Assuming there is a natural formal framework capturing human reasoning (I think the record so far suggests optimism) then there is something interesting that we don’t yet understand. It seems like you are applying the argument: “We know that humans can do X, so why do you think that X is an important problem?” The comment about undecidability issues not applying in practice also seems a bit unfair; for programs that do proof search we know that we cannot prove claims of the desired type based on simple Godelian arguments, and almost all interesting frameworks for reasoning are harder to prove things about than a simple proof search. (Of course the game is that we don’t want to prove things about the algorithms in question, we are happy to form justified beliefs about them in whatever way we can, including inductive inference. But the point is that there are things we don’t understand.)
There are further questions about whether any work at MIRI is a meaningful contribution to this problem or any other. I think that the stuff I’ve worked on is plausibly but not obviously a significant contribution (basically the same status as the other work I’m doing).
Regarding the modal agents stuff, I agree that it’s a toy problem where you should expect progress to be fast (if there was a nice theorem at the end of it, then it wouldn’t be too unusual as a paper in theoretical CS, except for the unfashionable use of mathematical logic). Regarding updateless/timeless/ambient decision theory, it’s a clear step forward for a very idiosyncratic problem, but one for which I think you can make a reasonable case that it’s worthwhile.
I think you shouldn’t be too surprised to make meaningful headway on theoretically interesting questions, even those which will plausibly be important. It seems like in theoretical research today things are still developing reasonably rapidly, and the ratio between plausibly important problems and human capital is very large. I expect that given effort and success at recruiting human capital MIRI can make good headway, in the same sort of way that other theorists do. Optimistically they would be distinguished primarily by working on a class of problems which is unusually important given their values and model of the world (a judgment with which you might disagree).
Of course the game is that we don’t want to prove things about the algorithms in question, we are happy to form justified beliefs about them in whatever way we can, including inductive inference. But the point is that there are things we don’t understand.
And the question is: who cares? The mechanism by which human beings predict their future behavior is not logical inference. Similar ad-hoc Bayesian extrapolation techniques can be used in any general AI without worry about Löbian obstacles. So why is it such a pressing issue?
I don't wish to take away fr...
Previously: Why Neglect Big Topics.
Why was there no serious philosophical discussion of normative uncertainty until 1989, given that all the necessary ideas and tools were present at the time of Jeremy Bentham?
Why did no professional philosopher analyze I.J. Good’s important “intelligence explosion” thesis (from 19591) until 2010?
Why was reflectively consistent probabilistic metamathematics not described until 2013, given that the ideas it builds on go back at least to the 1940s?
Why did it take until 2003 for professional philosophers to begin updating causal decision theory for the age of causal Bayes nets, and until 2013 to formulate a reliabilist metatheory of rationality?
By analogy to financial market efficiency, I like to say that “theoretical discovery is fairly inefficient.” That is: there are often large, unnecessary delays in theoretical discovery.
This shouldn’t surprise us. For one thing, there aren’t necessarily large personal rewards for making theoretical progress. But it does mean that those who do care about certain kinds of theoretical progress shouldn’t necessarily think that progress will be hard. There is often low-hanging fruit to be plucked by investigators who know where to look.
Where should we look for low-hanging fruit? I’d guess that theoretical progress may be relatively easy where:
These guesses make sense of the abundant low-hanging fruit in much of MIRI’s theoretical research, with the glaring exception of decision theory. Our September decision theory workshop revealed plenty of low-hanging fruit, but why should that be? Decision theory is widely applied in multi-agent systems, and in philosophy it’s clear that visible progress in decision theory is one way to “make a name” for oneself and advance one’s career. Tons of quality-adjusted researcher hours have been devoted to the problem. Yes, new theoretical advances (e.g. causal Bayes nets and program equilibrium) open up promising new angles of attack, but they don’t seem necessary to much of the low-hanging fruit discovered thus far. And progress in decision theory is definitely not valuable only to those with unusual views. What gives?
Anyway, three questions:
1 Good (1959) is the earliest statement of the intelligence explosion: “Once a machine is designed that is good enough… it can be put to work designing an even better machine. At this point an ”explosion“ will clearly occur; all the problems of science and technology will be handed over to machines and it will no longer be necessary for people to work. Whether this will lead to a Utopia or to the extermination of the human race will depend on how the problem is handled by the machines. The important thing will be to give them the aim of serving human beings.” The term itself, “intelligence explosion,” originates with Good (1965). Technically, artist and philosopher Stefan Themerson wrote a "philosophical analysis" of Good's intelligence explosion thesis called Special Branch, published in 1972, but by "philosophical analysis" I have in mind a more analytic, argumentative kind of philosophical analysis than is found in Themerson's literary Special Branch. ↩