How to study brains and minds

There is currently a fight going on in cog-neuro whose outcome GGers should care about. It is illuminatingly discussed in a recent paper by Krakauer, Ghazanfar, Gomez-Marin, MacIver and Poeppel (KGG-MMP) (here). The fight is about how to investigate the mind/brain connection. There are two positions. One, which I will call the “Wrong View” (WV) just to have a useful mnemonic, takes a thoroughly reductionist approach to the problem. The idea is that a full understanding of brain function will follow from a detailed understanding of “their component parts and molecular machinery” (480). The contrary view, which I dub the “Right View” (RV) (again, just to have a name),[1] thinks that reductionism will not get nearly as far as we need to go and that the only way to get a full understanding of how brains contribute to thinking/feeling/etc. requires neural implementations in tandem with (and more likely subsequent to) “careful theoretical and experimental decomposition of behavior.” More specifically, “the detailed analysis of tasks and of the behavior they elicit is best suited for discovering component processes and their underlying algorithms. In most cases,…the study of the neural implementation of behavior is best investigated after such behavioral work” (480). In other words, WV and RV differ not over the end game (an understanding of how the brain subvenes the brain mechanisms relevant to behavior) but the best route to that end. WV thinks that if you take care of the neuronal pennies, the cognitive dollars will take care of themselves. The RV thinks that doing so will inevitably miss the cognitive forest for the neural trees and might in fact even obscure the function of the neural trees in the cognitive forest. (God I love to mix metaphors!!). Of course, RV is right and WV is wrong. I would like to review some of the points KGG-MMP makes arguing this. However, take a look for yourself. The paper is very accessible and worth thinking about more carefully.

Here are some points that I found illuminating (along with some points of picky disagreement (or, how I would have put things differently)).

First, framing the issue as one of “reductionism” confuses matters. The issue is less reduction than it is a neurocentric myopia. The problem KGG-MMP identifies revolves around the narrow methods standard practice deploys not the ultimate metaphysics that it endorses. In other words, even if there is, ontologically speaking, nothing more than “neurons” and their interactions,[2] discovering what these interactions are and how they combine to yield the observed mental life will require well developed theories of this mental life expressed in mentalistic non-neural terms. The problem then with standard practice is not its reduction but its methodological myopia. And KGG-MMP recognizes this. The paper ends with an appeal for a more “pluralistic” neuroscience, not an anti-reductionist one.

Second, KGG-MMP gives a nice sketch of how WV has become so prevalent. It provides a couple of reasons. First, has been the tremendous success of “technique driven neuroscience” (481). There can be no doubt that there has been an impressive improvement in the technology available to study the brain at the neuronal level. New and better machines, new and better computing systems, new and better maps of where things are happening. Put these all together and it is almost irresistible to grab for the low hanging fruit that such techniques bring into focus. Nor, indeed should this urge be resisted. What needs resisting is the conclusion that because these sorts of data can be productively gathered and analyzed that these data suffice to answer the fundamental questions.

KGG-MMP traces the problem to a dictum of Monod’s: “what is true of the bacterium is true of the elephant.” KGG-MMP claims that this has been understood within cog-neuro as claiming that “what is true for the circuit is true for the behavior” and thus that “molecular biology and its techniques should serve as the model of understanding in neuroscience” (481).

This really is a pretty poor form of argument. It effectively denies the possibility of emergence. Here’s Martin Reese (here) making the obvious point:

Macroscopic systems that contain huge numbers of particles manifest ‘emergent’ properties that are best understood in terms of new, irreducible concepts appropriate to the level of the system. Valency, gastrulation (when cells begin to differentiate in embryonic development), imprinting, and natural selection are all examples. Even a phenomenon as unmysterious as the flow of water in pipes or rivers is better understood in terms of viscosity and turbulence, rather than atom-by-atom interactions. Specialists in fluid mechanics don’t care that water is made up of H₂O molecules; they can understand how waves break and what makes a stream turn choppy only because they envisage liquid as a continuum.

Single molecules of H₂O do not flow. If one is interested in fluid mechanics then understanding will come only by going beyond the level of the single molecule or atom. Similary if one is interested in the brain mechanisms underlying cognition or behavior then it is very likely that we will need to know a lot about how groups of fundamental neural elements interact, not just how one does what it does. So just as a single bird doesn’t flock, nor a single water molecule flow, nor a single gastric cell digest, so neither does a single brain particle (e.g. neuron) think. We will need more.

Before I get to what more, I should add here that I don’t actually think that Mondo meant what KGG-MMP take him to have meant. What Monod meant was that the principles of biology that one finds in the bacterium are the same as those that we find in the elephant. There is little reason to suppose, he suggested, that what makes elephants different from bacteria lies in their smallest parts respecting different physical laws. It’s not as if we expect the biochemistry to change. What KGG-MMP and Reese observe is that this does not mean that all is explained by just understanding how the fundamental parts work. This is correct, even if Monod’s claim is also correct.

Let me put this another way: what we want are explanations. And explanations of macro phenomena (e.g. flight, cognition) seldom reduce to properties of the basic parts. We can completely understand how these work without having the slightest insight into why the macro system has the features it does. Here is Reese again on reduction in physics:

So reductionism is true in a sense [roughly Monod’ sense, NH]. But it’s seldom true in a useful sense. Only about 1 per cent of scientists are particle physicists or cosmologists. The other 99 per cent work on ‘higher’ levels of the hierarchy. They’re held up by the complexity of their subject, not by any deficiencies in our understanding of subnuclear physics.

So, even given the utility of understanding the brain at the molecular level (and nobody denies that this is useful), we need more than WV allows for. We need a way of mapping two different levels of description onto one another. In other words, we need to solve what Embick and Poeppel have called the “granularity mismatch problem” (see here). And for this we need to find a way of matching up behavioral descriptions with neural ones. And this requires “fine grained” behavioral theories that limn mental mechanisms (“component parts and sub-routinges”) as finely as neural accounts describe brain mechanisms. Sadly, as KGG-MMP notes, behavioral investigation “has increasingly been marginalized or at best postponed” (481-2), and this has made moving beyond the WV difficult. Rectifying this requires treating behavior “as a foundational phenomenon in its own right” (482).[3]

Here is one more quibble before going forward. I am not really fond of the term ‘behavioral.’ What we want is a way of matching up cognitive mechanisms with neural ones. We are not really interested in explaining actual behavior but in explaining the causal springs and mechanisms that produce behavior. Focusing on behavior leads to competence/performance confusions that are always best avoided. That said, the term seems embedded in the cog-neuro literature (no doubt a legacy of psychology’s earlier disreputable behaviorist past) and cannot be easily dislodged. What KGG-MMP intends is that we should look for mental models and use these to explore neural models that realize these mental systems. Of course, we assume that mental systems yield behaviors in specific circumstances, but like all good scientific theories, the goal is to expose the mental causes behind the specific behavior and it is these mental causal factors whose brain realization we are interested in understanding.  The examples KGG-MMP gives show that this is the intended point.

Third, KGG-MMP nicely isolates why neuroscience needs mental models. Or as KGG-MMP puts is: “Why is it the case that explanations of experiments at the neural level are dependent on higher level vocabulary and concepts?” Because “this dependency is intrinsic to the very concept of a “mechanism”.” The crucial observation is that “the components of a mechanism do different things than the mechanism organized as a whole” (485). As Marr noted, feathers are part of the bird flight mechanism, but feathers don’t fly. To understand how birds fly requires more than a careful description of their feathers. So too with neurons.

Put another way, as mental life (and so behavior) is an emergent property of neurons how neurons subvene mental processes will not be readily apparent by only studying neural properties singularly or collectively.

Fourth, KGG-MMP gives several nice concrete examples of fruitful interactions between mental and neural accounts. I do not review them here save to say that sound localization in barn owls makes its usual grand appearance. However, KGG-MMP provides several other examples as well and it is always useful to have a bunch of these available on hand.

Last, KGG-MMP got me thinking about how GGish work intersects with the neuro concerns the paper raises, in particular minimalism and its potential impact for neuroscience. I have suggested elsewhere (e.g. here) that MP finally offers a way of bridging the granularity gap that Embick and Poeppel. The problem as they saw it, was that the primitives GGers were comfortable with (binding, movement, c-command) did not map well to primitives neuro types were comfortable with. If, as KGG-MMP suggests, we take the notion of the “circuit” as the key bridging notion, the problem with GG was that it did not identify anything simple enough to be a plausible correlate to a neural circuit. Another way of saying this is that theories like GB (though very useful) did not “dissect [linguistic, NH] behavior into its component parts or subroutines” (481). It did not carve linguistic capacity at its joints. What minimalism offers is a way of breaking GB parts down into simpler subcomponents. Reducing macro GB properties to products of simple operations like  Merge or Agree or Check Feature promises to provide mental parts simple enough to be neurally interpretable. As KGG-MMP makes clear finding the right behavioral/mental models matters and breaking complex mental phenomena down into its simpler parts will be part of finding the most useful models for neural realization.

Ok, that’s it. The paper is accessible and readable and useful. Take a look.

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[1] As we all know, the meaning of the name is just what it denotes so there is no semantic contribution that ‘wrong’ and ‘right’ make to WV and RV above.

[2] The quotes are to signal the possibility that Gallistel is right that much neuronal/cognitive computation takes place sub neuronally.

[3] Again, IMO, though I agree with the thrust of this position, it is very badly put. It is not behavior that is foundational but mentalistic accounts of behavior, the mechanisms that underlie it, that should be treated as foundational. In all cases, what we are interested in are the basic mechanisms not their products. The latter are interesting exactly to the degree that they illuminate the basic etiology.

Darwin's problem; some reasonable

Karthik Durvasula has pointed me to a thoughtful blog post by the Confused Academic (CA) critical of using Darwin’s Problem (DP) kind of considerations as a criterion in the evaluation of linguistic proposals (see here).[1] The main thrust of the (to repeat, very reasonable) points made is that we know very little about how evolutionary considerations apply to cognitive phenomena in general and linguistic phenomena in particular and, as such, we should not expect too much from DP kinds of considerations. Indeed, as I noted here, there are several problems with giving a detailed account how FL evolved. Let me remind you of some of the more serious issues, as CA adverts to similar ones.

The most obvious is the remove between cognitive powers and genetic ones. In particular, for an account of the evolution of FL we need a story of how minds are incarnated in brains and how brains are coded in genes. Why? Because evolution rejiggers genomes, which in turn grow brains, which in turn secrete cognition.  Sadly, every link of this chain is weak, most particularly in the domain of language (though the rest of cognition is not in much better shape as Lewontin’s famous piece (noted by CA) emphasizes). We really don’t know much about the genetic bases of brain development, nor do we know much about how brains realize FL. So, though we do know a fair bit about the cognitive structure of FL, we don’t have any really good linking hypotheses taking us from this to the brain and the genome, which are the structures that evolution manipulates to work its magic. In other words, to really explain how FL evolved (at least in detail) we need to account for how the brains structures that embody FL rose via alterations in our ancestors’ genomes (broadly construed to include epigenetic factors), and right now, though we have decent cognitive descriptions of FL, we have no good way of linking these up to brains and genes.

Second, if Lewontin is right (and I for one found his discussion entirely persuasive) then the prospects of giving standard evo accounts of how FL evolved will be largely nugatory due to the virtual impossibility of finding the relevant evidence, e.g. there really exist no “fossil” records to exploit and there is really nothing like our linguistic facility evident in any of our primate “cousins.” This makes constructing a standard evolutionary account empirically very dicey. 

In sum, things do not look good, so there arises the very reasonable question of what good DP thinking is for the practicing linguist. That’s the question CA asks. Here’s what I think (acknowledging that the problems CA notes are serious): Despite these problems, I still think that DP thinking is useful. Let me say why.

As I’ve noted (I suspect too many times) before (e.g. here) there is a tension between Plato’s Problem (PP) and DP. The former encourages packing as much as possible into UG to make the acquisition problem easier while the latter eschews this strategy to make the evolvability problem more tractable. Put another way: the more linguistic knowledge is given rather than acquired[2], the easier it is to account for why acquisition is as easy and effortless as it seems to be. However, the more there is packed into FL/UG the more challenging it is to explain how this knowledge could have evolved. This is the tension, and here is why I like DP: this tension is a creative one. These two problems together generate a very interesting theoretical problem: how to have one’s DP cake and PP’s too (i.e. how to allow for a solution to both PP and DP). I have suggested several strategies about how this might be accomplished that leads, IMO, to an interesting research program (e.g. here). My claim is that if you find this program attractive, then you need to take DP semi-seriously. What do I mean by “semi” here? Well, nobody expects to explain how FL actually evolved given how little we know about the relevant bridging assumptions (see above), but by thinking of the problem in tandem with PP we know the kinds of things we need to do (e.g. effectively eliminate the G internal modularity of characteristic of GB style theories and show that all the apparently different linguistic dependencies found outlined in the separate GB modules are effectively one and the same). That’s the first necessary step needed to reconcile DP and PP.[3]

The second, also motivated by DP, is yet more interesting (and challenging): to try and factor out those G operations, principles and primitives that are not linguistically specific. Thus, given DP we want not only a simpler (more elegant, more beautiful yadda, yadda, yadda) theory, but a particular kind of simpler etc. theory. We want one with as little linguistic specificity as possible. Maybe an example would help here.

The cyclic nature of derivations has long been a staple of GG theory. Ok, how to explain this? Earlier GG theory simply stipulated it: rules apply cyclically. The Minimalist Program (MP) has tried to offer slightly deeper motivation. There are two prominent accounts in the literature: the cycle as expression of the Extension Condition (EC) and the cycle as the expression of feature checking (Featural Cyclicity (FC)). FC is the idea that “bad” (unvalued or un-interpretable) features must be discharged quickly (e.g. in the phase or phrase that introduces them). EC says that derivations are monotonic (i.e. constituents that are inputs to a G operation must be constituents in the output of the operation).

There are various empirical linguistic-theory internal reasons that have been offered for preferring one or the other of these ideas. Both apply over a pretty general domain of cases and, IMO, it is hard to argue that either is in any relevant sense “simpler” than the other. However, IMO, the world would be a better place minimalistically were the EC the right way to conceptually ground the cycle. Why? Because it has the right generic feel to it because it looks like a very generic property of computations. In other words, IMO, it would be natural to find that cognitive rules systems in general are monotonic (information preserving) so that to find this holding of Gs would not be a surprise. FC, on the other hand, strikes me as relying on quite linguistically special assumptions about the toxicity of certain linguistic features and how quickly they need to be neutralized (some examples of very linguistically special properties: only probes contain toxic features, only phase heads have toxic features, toxic features must be very quickly eliminated, Gs contain toxic features at all). Personally, I find it hard to see FC and its special conception of features generalizing to other cognitive domains of third factor considerations. Of course I could be wrong (indeed given my track record, I am likely wrong!). What’s nice about a DP perspective is that it encourages us to try and make this kind of evaluation (i.e. ask how generic/specific a proposed operation/principle is) and, if my reasoning is on the right track, it suggests that we should try to maintain EC as a core feature precisely because it is plausibly not linguistic specific (i.e. not tied to special properties of human Gs).[4]

You could rightly object that such considerations are hardly dispositive, and I would agree. But if the above form of reasoning is even moderately useful, it suggests that DP considerations can have some theoretical utility. So, DP points to certain kinds of accounts and encourages one to develop theories with a certain look. It encourages the unification of GB modules and the elimination of linguistically specific features of Gs. It does this by highlighting the tension between DP and PP. One might construe all of this in simplicity terms, but from where I sit, DP encourages a very specific kind of simple, elegant theory (i.e. it favors some simple theories over others) and for this alone it earns its theoretical keep.[5]

CA has one other objection to DP that I would like to briefly touch on: DP encourages reductionism and reductionism is not a great methodological stance. I have two comments.

First, I am not personally against reduction if you can get it. My problem with it is that it very hard to come by, and I do not expect it to occur any day soon in my neck of the scientific woods. However, I do like unification and think that we should be encouraged to seek it out. As my good and great friend Elan Dresher once sagely noted: there are really only two kinds of linguistic papers. The first shows that two things that appear completely different are roughly the same. The second shows that two things that are roughly the same are in fact identical. I don’t know about linguistic papers in general, but this is a pretty good description of what a good many theory papers look like. Unification is the name of the game. So if by reduction we mean unification, then I am for it. Nothing wrong with it and a great deal that is right In fact, there is nothing wrong with real reduction either, if you can pull it off. Sadly, it is very very hard to do.

Second, I think that for MP to succeed then we should expect lots of reduction/unification. We will need to unify the modules (as noted above) and unify certain cognitive and computational operations. If we cannot manage this, then I would conclude that the main ideas/intuitions behind MP are untenable/unworkable/sterile. So, maybe unlike CA I welcome the reductionist/unificationist challenge.  Not only is this good science, DP is betting that it is the next important step for GG.

This said, there is something bad about reduction, and maybe this is what CA was worried about. Some reductionism takes it as obvious that the reducing science is more epistemologically privileged than the reduced one. But I see no reason for thinking that the metaphysics of the case (e.g. if A reduces to B) implies that the reducing theory is more solidly grounded epistemologically than the reduced one. So the fact that A might reduce to B does not mean that B is the better theory and that A’s results must bow to B’s theoretical diktats. Like all science, reduction/unification is a completed affair. It is best attempted when there is a reasonable body of doctrine in the theories to be related. I suspect that CA (and I am pretty sure Karthik) thinks that this is actually the main problem with DP at this time. It is premature (and if Lewontin is right, it will remain premature for the foreseeable future) precisely because of the problems I noted above concerning the assumptions required to bridge genes and cognition. My only response to this is that I am (slightly) more optimistic. I think DP considerations, even if inchoate, have purchase, though I agree that we should proceed carefully given how little we know of the details. So, we should make haste very very slowly.

Let me end. I think that DP has raised important questions for theoretical linguistics. Like most questions, they are yet somewhat undefined and fuzzy. Our job is to try and make them clearer and find ways of making them empirically viable. I believe that MP has succeeded in this to a degree. This said, CA (and Karthik) are right to point out the problems. Needless to say (or as I have said), I remain convinced that DPish considerations can and should play a role in how we develop theory moving forward for if nothing else (and IMO this is enough) it helps imbue the all to vague notions of elegance and simplicity with some local linguistic content. In other words, DP clarifies what kinds of elegant and simple theories of FL and UG we should be aiming for.

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[1] Importantly, CA is not anti minimalist and believes that general criteria like elegance and simplicity (suitably contextualized for linguistics) can play a useful role. It’s DP that bothers CA not theoretical desiderata on syntactic theories.

[2] Indeed the more linguistic specific this knowledge is, the easier it is to explain the facility of acquisition despite the limitations in the PLD for G construction.

[3] I should be careful here: it is conceptually possible that one small genetic change creates a brain that looks GBish. Recall, we really don’t know how a fold here and there in a brain unlocks cognition. But, if we assume that the small thing that happened genetically to change our brains resulted in a simple new cognitive operation being added to our previous inventory, we are home free. This seems like a reasonable assumption, though it might be wrong. Right now, it is the simplest least convoluted assumption. So it is a good place to start.

[4] To say what need not be said: none of this implies that EC is right and FC wrong. It means that EC has more MPish value than FC does if you share my views. So, if we want to pursue an MPish line of inquiry, then EC is a very good way to go. Or, you should demand lots of good empirical reasons for rejecting it. DP, like PP, when working well, conceptually orders hypotheses making some more desirable than others all things being equal.

[5] These considerations were prompted by a very fruitful e-mail exchange with Karthik. He pointed out that notions like simplicity etc., in order to be useful, need to be crafted to apply to a domain of inquiry. The above amounts to suggesting that DP helps in isolating the right kind of simplicity considerations.