In a nutshell, the authors scanned a group of dieting participants as they viewed and rated a series of foods that varied in their taste and health value. The dieters were classified into “self-control” (SC) and “no self-control” (NSC) groups based on their behavior during the task. The SC participants rejected foods that were unhealthy even if they liked those foods, whereas the NSC participants based their decisions to accept or reject foods based almost entirely on their taste value.

The imaging results tell a very similar story to the one Rangel’s group at Caltech has been promoting for a while now. To summarize:

• Ventromedial PFC (VMPFC) activation shows stronger responses to foods participants accept than foods they reject. In Hare et al’s terminology, it represents the “goal value” of the food.
• VMPFC likes tasty foods in all participants, but only likes healthy foods in SC participants.
• When trials that required self-control (i.e., those that offered tasty but unhealthy foods) were binned based on whether participants successfully exercised self-control (rejecting the item) or failed to exercise self-control (accepting the item), both groups of dieters showed activation in dorsolateral prefrontal cortex (DLPFC). But the SC dieters showed more activation.

So far so good. These are nice results, and while I don’t know that they’re Science-worthy, they’re at the very least consistent with the idea that (to put it simplistically) VMPFC tells us what we like, and DLPFC tells us whether or not we’re going to choose what we like. But of course, that interpretation (which shows up in the title of the paper) implies a stronger claim, namely, that DLPFC actually modulates the VMPFC representation. And here’s where things get a bit wobbly.

The first analysis Hare et al present to try and make the case that DLPFC and VMPFC are actually talking to each other is a simple correlational analysis demonstrating that DLPFC and VMPFC are inversely related across SC participants. Meaning, self-controllers who show relatively more DLPFC activation also show relatively less VMPFC activation.

While this first result is interesting, it’s not very convincing, for a couple of reasons. One is that there often are very large individual differences in global activation in fMRI studies, meaning that some people just systematically show more activation than others in regions that are task-positive, and more deactivation in regions that are task-negative. VMPFC and DLPFC fit the bill here, in that the former was strongly deactivated and the latter was strongly activated. So one would like to see some evidence of specificity here. Is this association selective to the DLPFC-VMPFC circuit, or are similar inverse correlations found between very diffuse brain networks? And similarly, is the correlation the authors report specific to self-control trials, or does it also show up for non self-control trials? The authors only report the former, and one would like to know that the latter didn’t hold (i.e., you shouldn’t see a correlation that’s supposedly related to self-control in a condition where there’s no need for self-control!).

A second and more serious concern is that the presence of a between-subject correlation between two regions really says almost nothing about whether those two regions are talking to one another in a meaningful way. What Hare et al want to argue is that, on a trial-by-trial basis, when DLPFC kicks in, VMPFC is downregulated, resulting in a behavioral change. In other words, changes in DLPFC activation cause changes in VMPFC activation. But demonstrating that people who show more activation in DLPFC on average also show less activation in VMPFC on average isn’t the same thing. There are any number of ways you could get a negative between-subject correlation between two regions without any within-subject correlation whatsoever. One trivial example I alluded to above is that some people might just be more engaged in the task than others. DLPFC and VMPFC tend to show a negative correlation in all kinds of tasks; one plausible interpretation for this is that people who pay more attention to the task will show more activation in “task-positive” regions and more deactivation in “task-negative” regions. So you could very well get this effect for free, no self-regulation required.

In any case, Hare et al go on to report a second “functional connectivity” analysis. Unlike the above correlational analysis (which, unfortunately, some people also refer to as a functional connectivity analysis), the functional connectivity analysis was conducted over time rather than over participants. In other words, Hare et al were looking for regions in which activation tended to covary with a “seed” region of interest (in this case, DLPFC). The rationale for this type of analysis is that if two regions tend to coactivate, it’s reasonable to suppose that there might be a causal relationship between them (though articulating that relationship is not so easy).

The big problem with functional connectivity analysis is that it’s very difficult to test whether the correlation between two regions differs reliably across conditions. Unfortunately, that’s often exactly what we want to know. In this case, what Hare et al want to show is that the correlation between DLPFC and VMPFC exists specifically during trials that require self-control (i.e., unhealthy foods), and isn’t always there (which would argue against a self-control-specific explanation). So they perform what’s called a psychophysiological interaction (PPI) analysis. The basic idea here is that you add a term into your model that codes for the interaction between the experimental variables you care about (e.g., healthy vs. unhealthy trials) and the activation in the seed region. (Statistically, this is just the product of the two variables, after controlling for their main effects.) You can then interpret any regions you identify through this analysis roughly as “regions that show a stronger correlation with the seed region in one condition than another”. In this case, Hare et al identify a number of regions that show functional connectivity with DLPFC.

Sounds good, right? If it’s this easy, why doesn’t everyone use PPI analysis? Unfortunately, there’s a big technical problem, which is that the BOLD response (the signal that fMRI detects) is kind of slow, and lags behind neuronal activation for several seconds. Without getting too deep into the details, what this basically means is that if you run a standard PPI analysis, as implemented in some fMRI packages, you actually aren’t identifying regions that covary with neural activation in your seed region. Instead, you’re identifying regions in which activation correlates with the delayed hemodynamic response in your seed region. Which, to put it bluntly, makes it very difficult to have any idea what you’re really looking at.

The solution some people have adopted to this problem is to use a very complicated deconvolution approach to essentially try and figure out what neural activity must have been like several seconds before the response you observed. Once you’ve done that, you then use that estimate of neural activity in your PPI analysis rather than the observed signal itself. After that, you can interpret the results in the relatively straightforwad way I suggest above, i.e., you can identify regions that show changes in functional connectivity with your seed region as a function of condition.

If this all sounds like black magic to you, you’re not alone. While opinions certainly vary, mine, for what it’s worth, is that PPI analyses are close to worthless. You have to make so many convoluted (no pun intended) assumptions about what activation must have been like to produce the observed signal, and what activation will probably be like if we just multiply this indicator variable by this time-series and pretend that everything remains perfectly stationary when we reconvolve it, and what the shape of the hemodynamic response is in all the other regions we’re correlating with the seed ROI, that it’s virtually impossible to come away feeling confident that you know what your results reflect. So, on purely methodological grounds, I think it’s reasonable to express a good deal of skepticism about any paper that bases its strongest claim on a very convoluted technique that really hasn’t been adequately validated.

Having said that, opinions do vary, and some people might feel perfectly comfortable with Hare et al’s analysis, had it produced the expected result–namely, that DLPFC activation correlations with VMPFC activation during evaluation of unhealthy foods, but not otherwise. But Hare et al don’t actually show that. What they find, instead, is that DLPFC is functionally connected to a number of other frontoparietal regions. You might think this to be a deal-break for the hypothesis; but the authors are persistent, and instead suggest that “DLPFC might modulate the vmPFC through its effect in a third region, such as IFG/BA46.”

It’s not immediately clear why this second hypothesis should be necessary; after all, the PPI analysis is acausal. It doesn’t tell you that DLPFC caused activation in VMPFC, it just tells you that the two are correlated. If there really was any sort of relation between DLFPC and VMPFC, however many nodes it was mediated by, you would still expect it to show up in the first analysis. If it doesn’t, you might want to conclude that any effect, however indirect, is relatively weak, and probably can’t account for the large differences in mean levels of activation in these regions.

In any case, to test their prediction, Hare et al then conduct a second PPI analysis, using the IFG region that was functionally connected with the original DLPFC seed as the new seed (minimal rationale for this choice is provided, and there were other available candidates, so it’s pretty clear this was a fishing expedition). This time they get lucky: the third region (IFG) was in fact functionally connected to the VMPFC. So Hare et al conclude that, indeed, “vmPFC was functionally connected to the left DLPFC through a two-node network”. Hypothesis confirmed!

In sum, the best evidence the authors have for their claim that “Self-Control in Decision-Making Involves Modulation of the vmPFC Valuation System” (the paper’s title) is that they were able to find a third region that appeared to be functionally connected to both DLPFC and VMPFC using some very methodologically convoluted analyses and a rather unprincipled approach to region selection. That’s my take on it, at least; I leave it to you to decide whether or not to believe the result.

Having said all that, I hasten to point out that I don’t think this is a bad study overall. Other than the connectivity analyses, the results are pretty compelling, and represent a nice addition to the growing literature (much of it from Rangel’s lab) highlighting the VMPFC as a central component of the brain’s valuation system. It’s just that Hare et al never really provide any convincing evidence for their central claim–a claim that, one suspects, is what got the paper accepted in Science (along with a credulous reviewer or two, perhaps).

Over the past several years, the momentum has shifted away from hard-core materialism. The brain seems less like a cold machine. It does not operate like a computer. Instead, meaning, belief and consciousness seem to emerge mysteriously from idiosyncratic networks of neural firings. Those squishy things called emotions play a gigantic role in all forms of thinking. Love is vital to brain development.

This paragraph is interesting, because it provides a nice summary of recent trends in neuroscience (everything but the first sentence is true) while simultaneously betraying a deep misunderstanding of the materialist worldview. Brooks holds up constructs like meaning, belief, and consciousness as if they were antithetical to the “hard-core” materialist worldview; but should it surprise anyone that meaning and belief emerge from “idiosyncratic networks of neural firings”? Do materialists quake in their boots at the thought that love plays a role in brain development? It shouldn’t, and they don’t. A good materialist (not just a ‘hard-core’ materialist, whatever that means, but any good one) takes these observations as self-evident. If you believe, as materialist neuroscientists do, that the brain is the proximal source all thought, feeling, and action, then you must believe that meaning and belief arise through the actions of neurons chattering with one another; you must believe that the nurturing effects on love on human development are mediated by changes in the brain. For Brooks, the notion that love might influence brain development appears to come as an epiphany; but really, what alternative is there? Does he suppose that the real materialists are the ones who would deny the existence of meanings, beliefs, consciousness, and love? If so, there aren’t any. Maybe there used to be, briefly, in the 1980s heyday of eliminative materialism; but those materialists were philosophers (e.g., the Churchlands), not neuroscientists, and it appears they’ve long seen the light and backed away from their stronger claims (e.g., that terms like “belief” are just conveniences of folk psychology, and don’t map onto anything real).

This fundamental misunderstanding of the central tenet of materialism gets played out repeatedly in Brooks’ op-ed (despite the fact that it’s only one page long). Consider the following assertion, which Brooks seems to take as evidence against ‘militant’ materialism:

First, the self is not a fixed entity but a dynamic process of relationships. Second, underneath the patina of different religions, people around the world have common moral intuitions.

These points are hard to dispute, but they certainly don’t constitute an argument against “militant atheism” or “hard-core materialism”, unless one takes these militant atheist materialists to be people who not only don’t believe in meaning, belief, consciousness, and love, but also think the self is a fixed entity and that there’s no such thing as a moral intuition. Now, I haven’t met any of these people, but they sound like fascinating individuals, if a bit odd.

Or take the following statement, which accurately describes ongoing research in certain areas of cognitive science, neuroscience, and genetics:

Researchers now spend a lot of time trying to understand universal moral intuitions. Genes are not merely selfish, it appears. Instead, people seem to have deep instincts for fairness, empathy and attachment.

Or this one:

Scientists have more respect for elevated spiritual states. Andrew Newberg of the University of Pennsylvania has shown that transcendent experiences can actually be identified and measured in the brain (people experience a decrease in activity in the parietal lobe, which orients us in space). The mind seems to have the ability to transcend itself and merge with a larger presence that feels more real.

From a descriptive standpoint, “Brooks gets the research essentially right,” as Kelly Bulkeley notes in a commentary over on the SSRC blogs. But why Brooks thinks such findings will soon lead to militant materialism falling by the wayside, I don’t know. I would have thought precisely the opposite, and so it seems, does Bulkeley:

To begin with, neuroscientist Andrew Newberg’s brain-imaging studies of meditation, highlighted by Brooks, can easily be used to confirm rather than disprove a materialist worldview. Newberg’s finding that people who are meditating have measurable decreases in parietal lobe activity fits perfectly with the idea advanced by Richard Dawkins and others that religious experience is a product of altered or abnormal brain functioning. Contrary to the popular view that Newberg’s research supports religion, it can readily be taken as supporting the “militant atheism” Brooks wants to reject. The mind may, as Brooks says, have “the ability to transcend itself,” but we didn’t need Newberg’s SPECT scanners to tell us that.

This conclusion seems exactly right to me. After all, it would surely be better for non-materialists if it turned out that religious experiences didn’t have some identifiable neural correlates. “Look,” one could imagine them saying then, “visual perception, motor control, and speech production… all of these things depend on the brain. But transcendental experiences don’t!” Unfortunately, it doesn’t work out that way. Religious experiences turn out to have underlying neural representations, just like every other psychological state or process that’s been investigated. That includes meaning, belief, consciousness, and yes, love. Such findings aren’t inconsistent with materialism; they’re necessary for materialism to hold. Why this simple observation baffles Brooks so, I don’t know.

Having said all that, I do think there’s one redeeming point to Brooks’ Op-Ed. I think he has it basically right when he suggests that “we’re in the middle of a scientific revolution” that’s going to have “big cultural effects”. But I suspect that he’s banking on the wrong revolution. Instead of modern neuroscience giving rise to “neural Buddhism”, what’s much more likely to happen is that, as our understanding of the brain increases and we learn more and more about precisely those aspects of human behavior and cognition that were once thought to be resistant to material explanation, it’ll become increasingly difficult for non-materialists to adhere to their dogmas in the face of reductive explanations. In a world where religious experiences are scientifically mysterious, a dualist worldview is defensible, because there’s no better explanation than “God did it”. In a world where such experiences unfold as, say, a sequence of attractor states in a temporoparietal network that mediates the experience of agency, one has a choice between “God did it” and “the brain did it”. My bet is that, for many (though certainly not all) people, the brain will beat God.