I vastly disagree. I will just state it for now, and hopefully this will be a commitment to explain it further when I have the time. Here are my unjustified assertions about the nature of philosophy regarding OP's topics:
Philosophy has the most huge search space known to man, it encompasses everything (a) without a good clear-cut solution and (b) which has any hope to be solved (this rules out two extremes: science and religion).
Philosophy, by its very nature, has few systematized methods for efficient search. Seems like we discovered logical and clear thinking recently, but that's almost about it.
Because it is so difficult, philosophy is wrong 99,9% of the time.
When philosophy is right, major breakthroughs are made, sciences are created, new reasoning tools, higher moral standards and so on.
There's a massive and astronomical hindsight bias. Once solved a problem is no longer on the realm of philosophy and the solution tend to seem extremely obvious after 1 or 2 generations.
Thus, low hanging fruits in philosophy are nowhere to be found. Most of your examples were already found, they just need to be worked on. I chalenge you to present a yet unknown low hanging fruit, one all your peers don't know it already, one which would knock Nick's socks off.
I will second this. It's not that the process of theoretical discovery is inefficient due to any fault of its own, it's that the problem is intractable (e.g. we don't know how to do better than exhaustive search). So that linear looking search path from concept A to concept B did not take linear time to find...
Luke,
I think you are mistaken about the relative efficiency / inefficiency of scientific research. I believe that research is comparably efficient to much of industry, and that many of the things that look like inefficiencies are actually trading off small local gains for large global gains. I've come to this conclusion as the result of years of doing scientific research, where almost every promising idea I've come up with (including some that I thought quite clever) had already been explored by someone else. In fact, the typical case for when I was able to make progress was when solving the problem required a combination of tools, each of which individually was relatively rare in the field.
For instance, my paper on stochastic verification required: (i) familiarity of sum-of-squares programming; (ii) the application of supermartingale techniques from statistics; and (iii) the ability to produce relatively non-trivial convex relaxations of a difficult optimization problem. In robotics, most people are familiar with convex optimization, and at least some are familiar with sum-of-squares programming and supermartingales. In fact, at least one other person had already published a fairl...
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 infe...
Jacob, have you seen Luke's interview with me, where I've tried to reply to some arguments of the sort you've given in this thread and elsewhere?
I don't think [the fact that humans' predictions about themselves and each other often fail] is sufficient to dismiss my example. Whether or not we prove things, we certainly have some way of reasoning at least somewhat reliably about how we and others will behave. It seems important to ask why we expect AI to be fundamentally different; I don't think that drawing a distinction between heuristics and logical proofs is sufficient to do so, since many of the logical obstacles carry over to the heuristic case, and to the extent they don't this seems important and worth grappling with.
Perhaps here is a way to get a handle on where we disagree: Suppose we make a whole-brain emulation of Jacob Steinhardt, and you start modifying yourself in an attempt to achieve superintelligence while preserving your values, so that you can save the world. You try to go through billions of (mostly small) changes. In this process, you use careful but imperfect human (well, eventually transhuman) reasoning to figure out which changes are sufficiently safe to ...
I thought the example was pretty terrible.
Glad to see you're doing well, Benja :)
Sorry for being curmudgeonly there -- I did afterwards wish that I had tempered that. The thing is that when you write something like
I also agree that the idea of "logical uncertainty" is very interesting. I spend much of my time as a grad student working on problems that could be construed as versions of logical uncertainty.
that sounds to me like you're painting MIRI as working on these topics just because it's fun, and supporting its work by arguments that are obviously naive to someone who knows the field, and that you're supporting this by arguments that miss the point of what MIRI is trying to say. That's why I found the example of program analysis so annoying -- people who think that the halting problem means that program analysis is impossible really are misinformed (actually Rice's theorem, really, but someone with this misconception wouldn't be aware of that), both about the state of the field and about why these theorems say what they say. E.g., yes, of course your condition is undecidable as long as there is any choice f(s) of chooseAction2(s) that satisfies it; proof: le...
Regardless of why the opportunity has presented itself, can we hope that the MIRI research team and associated researchers will use (or are using) the fact that "visible progress in decision theory is one way to “make a name” for oneself" and proceed to do so? Seems like pretty low-hanging status-fruit given the team's progress so far.
For MIRI, the hard part is writing up the results in a way that appeals to philosophers. That's a highly specialized skill, and not one we've focused on hiring for (at our current budget). We tried to pay Rachael Briggs $20k to do it, since she had two decision theory papers selected for the Philosopher's Annual, but it was too work-intensive even for her. I think it would drive Eliezer mad to write in that style. I suspect I could do it, but it would take a lot of my time. I might be able to persuade Preston Greene to do it some day. Or maybe Kenny Easwaran, who attended our September 2013 decision theory workshop.
If possible, I'd be curious to hear more details about why Briggs found it too work-intensive. Her giving up on it was definitely not an outcome I would have predicted.
Maybe the difficulties that you face are part of the answer to the question of why theoretical progress doesn't happen faster.
After a paper published in 2011: "[Original draft was available in 2003. Hurrah for academic publishing. One journal reviewed the manuscript for nearly two years before determining that it was too long. No wonder philosophy has not advanced farther in the past 2,500 years.] "
Just wanted to mention that Physics is not immune to this. Bell's theorem requires only a first-year college math skill, yet it took 30 odd years after EPR to formulate it. Not even Einstein himself was able do it. Event horizons and inescapability of singularity required virtually no new math beyond 1917, yet it took some 50 years for the physicists to understand the picture. There are clearly some mental blocks people have which take decades and new generations to overcome.
Charles Fort, Lo!: "If human thought is a growth, like all other growths, its logic is without foundation of its own, and is only the adjusting constructiveness of all other growing things. A tree can not find out, as it were, how to blossom, until comes blossom-time. A social growth cannot find out the use of steam engines, until comes steam-engine-time. For whatever is supposed to be meant by progress, there is no need in human minds for standards of their own: this is in the sense that no part of a growing plant needs guidance of its own devising, ...
Some examples of a different kind of inefficiency, from AntiFragile:
...It struck me how lacking in imagination we are: we had been putting our suitcases on top of a cart with wheels, but nobody thought of putting tiny wheels directly under the suitcase. Can you imagine that it took close to six thousand years between the invention of the wheel (by, we assume, the Mesopotamians) and this brilliant implementation (by some luggage maker in a drab industrial suburb)? And billions of hours spent by travelers like myself schlepping luggage through corridors full
I think conformity effects play a huge role in this area. The large majority of modern philosophers all have similar educational and cultural backgrounds. They go to elite universities. They read the standard Western philosophical canon. They work very hard to publish a lot of papers in prestigious journals. They are friends with other academics and with other high achievers in the "standard" fields like finance, law, and medicine. Their parents were probably academics or from the upper middle class. They have spent most of their lives in a university setting.
If I had to take an honest guess? Theoretical discovery will behave "inefficiently" when it requires a breadth-first (or at least, breadth-focused) search through the idea space before you can find things that "fit together". Only once you have a bunch of things which "fit together" can you look at the shape of the "hole in idea-space" they all border, dive to the bottom of that lake, and bring up an entirely new idea which links them or unifies them.
So:
1) Mostly agreed, as described above.
2) As described above. M...
It strikes me that there's a second set of reasons that read something like:
See: the free will problem.
Normative uncertainty does not seem particularly interesting. You can just use set multiplication over probable futures and evaluations of them, and wind up with a regular problem with certain evaluations. It even agrees with normal methods if you assume a single, certain evaluation.
Now, as a concept it's important - realizing that you might not know what you want is a tremendous source of uncertainty that is easy to overlook. I just don't think that any new concepts or mathematical tools are needed to tackle it.
Do you agree about the relative inefficiency of theoretical discovery?
In presence, yes. In degree, no. Even the efficient market hypothesis presumes (indeed, requires) some delay inefficiencies, and even restricting to fields where economic incentives are very, very high we see some pretty significant delay inefficiencies.
The modern containerization revolution is dependent on certain types of math and metallurgy being available, but the underlying tools were probably available before the first world war (and, indeed, would have been even more useful...
Some examples of a different kind of inefficiency, from AntiFragile:
It struck me how lacking in imagination we are: we had been putting our suitcases on top of a cart with wheels, but nobody thought of putting tiny wheels directly under the suitcase. Can you imagine that it took close to six thousand years between the invention of the wheel (by, we assume, the Mesopotamians) and this brilliant implementation (by some luggage maker in a drab industrial suburb)? And billions of hours spent by travelers like myself schlepping luggage through corridors full of rude customs officers. Worse, this took place three decades or so after we put a man on the moon.
...The story of the wheel itself is even more humbling than that of the suitcase: we keep being reminded that the Mesoamericans did not invent the wheel. They did. They had wheels. But the wheels were on small toys for children. It was just like the story of the suitcase: the Mayans and Zapotecs did not make the leap to the application. They used vast quantities of human labor, corn maize, and lactic acid to move gigantic slabs of stone in the flat spaces ideal for pushcarts and chariots where they built their pyramids. They even rolled them on logs of wood. Meanwhile, their small children were rolling their toys on the stucco floors (or perhaps not even doing that, as the toys might have been solely used for mortuary purposes).
The same story holds for the steam engine: the Greeks had an operating version of it, for amusement, of course: the aeolipyle, a turbine that spins when heated, as described by Hero of Alexandria. But it took the Industrial Revolution for us to discover this earlier discovery.
nobody thought of putting tiny wheels directly under the suitcase
For the perfectly valid reason that tiny wheels are useless unless you have a really even and smooth surface to roll them on.
Imagine the usefulness of a wheeled suitcase on farm. Or even on cobblestones -- how long do you think these tiny wheels will survive?
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. ↩