Right, but most neuroscientists do not sit down and describe the inputs and outputs to the problem that they're studying. They're more driven by say, putting a mouse in a learning task and recording as many neurons possible, or asking if Gene X is required for the learning task, and so on. These are the kinds of statements that their experiments generate.
Chomsky: That's right..
Is that conceptually flawed?
Chomsky: Well, you know, you may get useful information from it. But if what's actually going on is some kind of computation involving computational units, you're not going to find them that way. It's kind of, looking at the wrong lamp post, sort of. It's a debate... I don't think Gallistel's position is very widely accepted among neuroscientists, but it's not an implausible position, and it's basically in the spirit of Marr's analysis. So when you're studying vision, he argues, you first ask what kind of computational tasks is the visual system carrying out. And then you look for an algorithm that might carry out those computations and finally you search for mechanisms of the kind that would make the algorithm work. Otherwise, you may never find anything. There are many examples of this, even in the hard sciences, but certainly in the soft sciences. People tend to study what you know how to study, I mean that makes sense. You have certain experimental techniques, you have certain level of understanding, you try to push the envelope -- which is okay, I mean, it's not a criticism, but people do what you can do. On the other hand, it's worth thinking whether you're aiming in the right direction. And it could be that if you take roughly the Marr-Gallistel point of view, which personally I'm sympathetic to, you would work differently, look for different kind of experiments.
Right, so I think a key idea in Marr is, like you said, finding the right units to describing the problem, sort of the right "level of abstraction" if you will. So if we take a concrete example of a new field in neuroscience, called Connectomics, where the goal is to find the wiring diagram of very complex organisms, find the connectivity of all the neurons in say human cerebral cortex, or mouse cortex. This approach was criticized by Sidney Brenner, who in many ways is [historically] one of the originators of the approach. Advocates of this field don't stop to ask if the wiring diagram is the right level of abstraction -- maybe it's not, so what is your view on that?
Chomsky: Well, there are much simpler questions. Like here at MIT, there's been an interdisciplinary program on the nematode C. elegans for decades, and as far as I understand, even with this miniscule animal, where you know the wiring diagram, I think there's 800 neurons or something ...
I think 300..
Chomsky: ...Still, you can't predict what the thing [C. elegans nematode] is going to do. Maybe because you're looking in the wrong place.
I'd like to shift the topic to different methodologies that were used in AI. So "Good Old Fashioned AI," as it's labeled now, made strong use of formalisms in the tradition of Gottlob Frege and Bertrand Russell, mathematical logic for example, or derivatives of it, like nonmonotonic reasoning and so on. It's interesting from a history of science perspective that even very recently, these approaches have been almost wiped out from the mainstream and have been largely replaced -- in the field that calls itself AI now -- by probabilistic and statistical models. My question is, what do you think explains that shift and is it a step in the right direction?
Chomsky: I heard Pat Winston give a talk about this years ago. One of the points he made was that AI and robotics got to the point where you could actually do things that were useful, so it turned to the practical applications and somewhat, maybe not abandoned, but put to the side, the more fundamental scientific questions, just caught up in the success of the technology and achieving specific goals.
So it shifted to engineering...
Chomsky: It became... well, which is understandable, but would of course direct people away from the original questions. I have to say, myself, that I was very skeptical about the original work. I thought it was first of all way too optimistic, it was assuming you could achieve things that required real understanding of systems that were barely understood, and you just can't get to that understanding by throwing a complicated machine at it. If you try to do that you are led to a conception of success, which is self-reinforcing, because you do get success in terms of this conception, but it's very different from what's done in the sciences. So for example, take an extreme case, suppose that somebody says he wants to eliminate the physics department and do it the right way. The "right" way is to take endless numbers of videotapes of what's happening outside the video, and feed them into the biggest and fastest computer, gigabytes of data, and do complex statistical analysis -- you know, Bayesian this and that [Editor's note: A modern approach to analysis of data which makes heavy use of probability theory.] -- and you'll get some kind of prediction about what's gonna happen outside the window next. In fact, you get a much better prediction than the physics department will ever give. Well, if success is defined as getting a fair approximation to a mass of chaotic unanalyzed data, then it's way better to do it this way than to do it the way the physicists do, you know, no thought experiments about frictionless planes and so on and so forth. But you won't get the kind of understanding that the sciences have always been aimed at -- what you'll get at is an approximation to what's happening.
And that's done all over the place. Suppose you want to predict tomorrow's weather. One way to do it is okay I'll get my statistical priors, if you like, there's a high probability that tomorrow's weather here will be the same as it was yesterday in Cleveland, so I'll stick that in, and where the sun is will have some effect, so I'll stick that in, and you get a bunch of assumptions like that, you run the experiment, you look at it over and over again, you correct it by Bayesian methods, you get better priors. You get a pretty good approximation of what tomorrow's weather is going to be. That's not what meteorologists do -- they want to understand how it's working. And these are just two different concepts of what success means, of what achievement is. In my own field, language fields, it's all over the place. Like computational cognitive science applied to language, the concept of success that's used is virtually always this. So if you get more and more data, and better and better statistics, you can get a better and better approximation to some immense corpus of text, like everything in The Wall Street Journal archives -- but you learn nothing about the language.