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pjeby comments on The usefulness of correlations - Less Wrong
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Fair enough.
It's hard to define explicitly what I'd consider a novel or surprising result, because— as you point out— mainstream psychology doesn't appear to have a unified reductionistic model of cognition, just an array of identified results and sub-models. I've thus made that requirement more charitable, changing it from "something novel or surprising" to the lower standard of "good modeling by control theory of a cognitive phenomenon", excluding motor response and some games (like a fielder catching a fly ball) in which acting externally like a simple control system is an easy and successful strategy.
By "motor response" I mean just the way that the actual nerves and muscles can vary their particular actions, while not changing the conscious description of what I'm doing. For example, I assign significant probability that a simple control circuit can be found that neatly fits the actions of my leg muscles (or the nerve signals that connect to them) when I'm walking and keeping my balance. I would, however, find it much less probable that a similarly simple control circuit fits my pattern of working vs. procrastinating. (Since control circuits are apparently Turing-complete, of course there's going to be some control circuit that matches it, but in the case of balance I think there's probably one with few enough parameters that it compresses the data effectively, compared to other models; while in the case of akrasia I doubt this.)
So I would count work vs. procrastination, or prescription errors, or charitable donations, or changing beliefs, as just a few examples of cognitive phenomena. Something like variation in libido over time, though, wouldn't surprise me as much if I find a control circuit model for it (though it would surprise me more than the balance example). I think it's fair to ask PCT for experimental evidence in the cognitive domain, since the way you diagnose and prescribe around here seems to presuppose some rather simple control circuits in cognitive phenomena.
As for considering direct introspection rather than experimental evidence, I'm rather mistrustful of what I consciously intuit about my own mind, since conscious awareness seems to be often distorted for signaling purposes, and since the false perception of religious experience (which I really wanted to be genuine) was one thing that kept me religious longer than I should have been. At this point, I strongly prefer experimental evidence.
With that said, could you read Marken's paper and tell me whether you stand behind it in the terms I asked above?
Now that I've read it, I have to say I agree with you: it is not good evidence. At best, it's an application of PCT to generate an interesting hypothesis or two.
I'm not sure why you'd expect akrasia to be a simple circuit. If it were a simple conflict, between exactly two things, you'd likely be able to resolve it consciously without much effort. A few weeks ago, I did a workshop where we charted a portion of one person's control structure in the area of not working on the iPhone app they wanted to write. It took a couple hours and filled most of a page with the relevant cognitive-level variables and their interconnections.
This is quite consistent with e.g. Ainslie's model of akrasia as involving multiple competing "interests"; I see PCT as an improvement over Ainslie in providing a straightforward implementation mapping, plus simplified management of Ainslie's notion of "appetites", which is not very well worked out (IMO) and a little too handwavy.
Replacing Ainslie's idea of "interests" having "appetites" with controllers measuring time-averaged variables seems like a straightforward win: instead of two entities, you have just one entity that's structurally similar to things we know our brains/nervous systems already have. (Also, Ainslie has no worked-out model for how prioritization and agreement between interests occur; PCT on the other hand has hierarchy and reference levels to account for them.)
Individually, the circuits are simple; collectively, the networks are not. I used to think things were simpler than they are, because I focused only on the things (functional beliefs) that were effectively connections between control circuits. I rarely addressed the settings of the circuits themselves, or used them as a springboard to identifying other beliefs or variables.
There's a difference between having a false label applied to a true experience, and having a false experience. The existence of perceptions such as "how much work I've gotten done lately" or "how much fun I'm having" is certainly some evidence for PCT's notion of time-averaged perceptual variables that can influence decision-making. It's also parsimonious to assume that the brain is unlikely to have evolved specific circuits for these perceptions, rather than simply having a basis for acquiring new perceptions.
In effect, the PCT model of cognitive variables explains how we represent all the things we "just know" or "just feel", including expert intuition in specialized subjects. The PCT prediction would be that if someone is skilled enough in a subject to have a specific intuition about something, we should be able to find a specific neural signal whose intensity corresponds to the degree of that intuition, and which is a time-averaged function of other (possibly gated) input signals.
I don't see how any of this seems extraordinary or controversial in the slightest, on the perception side.
Control, perhaps, might be more controversial... especially given the implication that we don't control our own actions directly, but can only do so through interaction with the control network. But for me, that implication is uncontroversial, because I've been writing about that (independently formed) idea since 2005.
Powers hypothesizes that "awareness" simply is a debugger that can go in and inspect any part of the network, injecting settings or testing hypotheticals. Anything we do by direct conscious intention would therefore consist of "manually" setting control values in the network, which of course would have no long-term effect if a higher-level controller puts the settings right back when you're done. What's more, if your conscious meddling is interfering with something in an "important" (high) position in the network, it's likely to reorganize in such a way that you no longer want to meddle with the network in that particular way!
And that actually sounds like the most straightforward explanation of akrasic behaviors, ever, and is also 100% consistent with everything I've already previously observed about mind hacking.
That is, we really don't control our own behaviors: our networks do. Free will is really just a special case, even if it doesn't seem that way at first glance. PCT just offers a better explanation than my rough models had for why/how that works.
Good. The experiment is, however, very good evidence for the hypothesis that R.S. Marken is a crank, and explains the quote from his farewell speech that didn't make sense to me before:
The basic problem is that, generically, if your model uses more free parameters than data points, then it is mathematically trivial that you can get an exact fit to your data set, regardless of what the data are: thus you've provided exactly zero Bayesian evidence that your model fits this particular phenomenon.
(This is precisely the case in the paper you pointed me to. Marken asserts that his model successfully predicts the overall and relative error rates with high precision; but if these rates had been replaced with arbitrary numbers before being fed to him, he would have come up with different experimental values of the parameters, and claimed that his model exactly predicted the new error rates! This is known around here as an example of a fake explanation.)
The fact that Marken was repeatedly told this, interpreted it to mean that others were jealous of his precision, and continued to produce experimental "results" of the same sort along with bold claims of their predictive power, makes him a crank.
Anyhow...
The point I keep stressing is that, if cognitive-domain PCT is precise enough to do treatment with, then it can't be bereft of experimental consequences; and no matter how appealing certain aspects of it might be intuitively, a lack of experimental support after 35 years looks pretty damning. If every cognitive circuit is so complicated that you can't make an observable prediction (about an individual in varying circumstances, or different people in the same circumstances, etc) without assuming more parameters than data points... then PCT doesn't actually teach you anything about cognition, any more than the physicists who ascribed fire and respiration to phlogiston actually learned anything from their theory.
You've pointed me to one experiment, which turned out to be the work of a crank; I've accordingly lowered the probability that PCT is valid in the cognitive domain, not because the existence of a crank proves anything against their hypothesis, but because that was the most salient experimental result that you could point to!
I'm still quite able to revise my probability estimate upwards if presented with a legitimate experimental result, but at the moment PCT is down in the "don't waste your time and risk your rationality" bin of fringe theories.
I'm not sure I follow you. I didn't get the impression that Marken's model had more tunable parameters than there were data points under study, or that it actually was tunable in such a way as to create any desired result.
I don't follow how this is the case. If I establish that a person is controlling for, say, "having a social life", and I know that one of the sub-controlled perceptions is "being on Twitter", then I can predict that if I interfere with their twitter usage they'll try to compensate in some way. I can also observe whether a person's behavior matches their expressed priorities -- i.e., akrasia -- and attempt to directly identify the variables they're controlling.
If at this point, you say that this is "obvious" and not supportive of PCT, then I must admit I'm still baffled as to what sort of result we should expect to be supportive of PCT.
For example, let's consider various results that (ISTM) were anticipated to some extent by PCT. Dunning-Kruger says that people who aren't good at something don't know whether they're doing it well. PCT said - many years earlier, AFAICT - that the ability to perceive a quality must inevitably precede the ability to consistently control that quality.
Which directly implies that "people who are good at something must have good perception of that thing", and "people who are poor at perceiving something will have poor performance at it."
That's not quite D-K, of course, but it's pretty good for a couple decades ahead of them. It also pretty directly implies that people who are the best at something are more likely to be aware of their errors than anyone else - a pretty observable phenomenon among high performers in almost any field.
This baffles me, since AFAICT you previously agreed that it appears valid for "motor" functions, as opposed to "cognitive" ones.
I consider this boundary to be essentially meaningless myself, btw, since I find it almost impossible to think without some kind of "motor" movement taking place, even if it's just my eyes flitting around, but more often, my hands and voice as well, even if it's under my breath.
It's also not evolutionarily sane to assume some sort of hard distinction between "cognitive" and "motor" activity, since the former had to evolve from some form of the latter.
In any event, the nice thing about PCT is that it is the most falsifiable psychological model imaginable, since we will sooner or later get hard results from neurobiology to confirm its truth or falsehood at successively higher levels of abstraction. As has previously been pointed out here, neuroscience has already uncovered four or five of PCT's expected 9-12 hardware-distinctive controller levels. (I don't know how many of these were known about at the time of PCT's formulation, alas.)
In the section "Quantitative Validation", under Table 1, it says (italics mine):
As you vary each speed component within the model, the fraction of errors by that component varies all the way from 0 to 1, rather independently of each other. Thus for any empirical or made-up distribution of the four error types, Marken would have calculated values for his four parameters that caused the model to match the four data points; so despite his claims, the empirical data offer literally zero evidence in favor of his model. Ditto with his claim that his model predicts the overall error rate.
I'll get to the rest of this later.