↑ comment by So8res ·
2015-06-11T23:08:59.014Z · EA(p) · GW(p)
That post mixes a bunch of different assertions together, let me try to distill a few of them out and answer them in turn:
One of Peter's first (implicit) points is that AI alignment is a speculative cause. I tend to disagree.
Imagine it's 1942. The Manhattan project is well under way, Leo Szilard has shown that it's possible to get a neutron chain reaction, and physicists are hard at work figuring out how to make an atom bomb. You suggest that this might be a fine time to start working on nuclear containment, so that, once humans are done bombing the everloving breath out of each other, they can harness nuclear energy for fun and profit. In this scenario, would nuclear containment be a "speculative cause"?
There are currently thousands of person-hours and billions of dollars going towards increasing AI capabilities every year. To call AI alignment a "speculative cause" in an environment such as this one seems fairly silly to me. In what sense is it speculative to work on improving the safety of the tools that other people are currently building as fast as they can? Now, I suppose you could argue that either (a) AI will never work or (b) it will be safe by default, but both those arguments seem pretty flimsy to me.
You might argue that it's a bit weird for people to claim that the most effective place to put charitable dollars is towards some field of scientific study. Aren't charitable dollars supposed to go to starving children? Isn't the NSF supposed to handle scientific funding? And I'd like to agree, but society has kinda been dropping the ball on this one.
If we had strong reason to believe that humans could build strangelets, and society were pouring billions of dollars and thousands of human-years into making strangelets, and almost no money or effort was going towards strangelet containment, and it looked like humanity was likely to create a strangelet sometime in the next hundred years, then yeah, I'd say that "strangelet safety" would be an extremely worthy cause.
How worthy? Hard to say. I agree with Peter that it's hard to figure out how to trade off "safety of potentially-very-highly-impactful technology that is currently under furious development" against "children are dying of malaria", but the only way I know how to trade those things off is to do my best to run the numbers, and my back-of-the-envelope calculations currently say that AI alignment is further behind than the globe is poor.
Now that the EA movement is starting to look more seriously into high-impact interventions on the frontiers of science & mathematics, we're going to need to come up with more sophisticated ways to assess the impacts and tradeoffs. I agree it's hard, but I don't think throwing out everything that doesn't visibly pay off in the extremely short term is the answer.
Alternatively, you could argue that MIRI's approach is unlikely to work. That's one of Peter's explicit arguments: it's very hard to find interventions that reliably affect the future far in advance, especially when there aren't hard objective metrics. I have three disagreements with Peter on this point.
First, I think he picks the wrong reference class: yes, humans have a really hard time generating big social shifts on purpose. But that doesn't necessarily mean humans have a really hard time generating math -- in fact, humans have a surprisingly good track record when it comes to generating math!
Humans actually seem to be pretty good at putting theoretical foundations underneath various fields when they try, and various people have demonstrably succeeded at this task (Church & Turing did this for computing, Shannon did this for information theory, Kolmogorov did a fair bit of this for probability theory, etc.). This suggests to me that humans are much better at producing technical progress in an unexplored field than they are at generating social outcomes in a complex economic environment. (I'd be interested in any attempt to quantitatively evaluate this claim.)
Second, I agree in general that any one individual team isn't all that likely to solve the AI alignment problem on their own. But the correct response to that isn't "stop funding AI alignment teams" -- it's "fund more AI alignment teams"! If you're trying to ensure that nuclear power can be harnessed for the betterment of humankind, and you assign low odds to any particular research group solving the containment problem, then the answer isn't "don't fund any containment groups at all," the answer is "you'd better fund a few different containment groups, then!"
Third, I object to the whole "there's no feedback" claim. Did Kolmogorov have tight feedback when he was developing an early formalization of probability theory? It seems to me like the answer is "yes" -- figuring out what was & wasn't a mathematical model of the properties he was trying to capture served as a very tight feedback loop (mathematical theorems tend to be unambiguous), and indeed, it was sufficiently good feedback that Kolmogorov was successful in putting formal foundations underneath probability theory. We're trying to do something similar with various other confusing aspects of good reasoning (such as logical uncertainty), and you're welcome to raise concerns about whether we need to understand good reasoning under logical uncertainty in order to build an aligned AI, but saying that there's "no feedback loop" seems to just misunderstand the approach.