• fMRI studies tell us what’s true of brain activation on the average, but we’re nowhere near the point where fMRI scans have diagnostic value at the level of individual subjects. Put another way, you may be able to tell that people with ADHD have somewhat different neural responses than people without ADHD on average, but you can’t tell whether someone has ADHD or not by looking at their individual brain activation.
• The functional implications of specific differences in brain activation are not always clear. If schizophrenics show more activation in frontal brain regions than healthy controls, is that a good or bad thing? Are the increases reflective of the underlying disorder, or do they represent the brain’s attempt to compensate for the underlying deficit? We just don’t know at this point.
• Scientists and journalists alike are too quick to draw what Poldrack has called the “reverse inference“, arguing that a specific cognitive function must be involved in a certain task on the basis of the spatial location of activation. For example, many researchers who observe increased amygdala activation in response to a particular stimulus are quick to suggest that people are engaging in emotional processing, when in fact the amygdala may be activated by many other types of processes. There just isn’t enough evidence to support most reverse inferences.
• For all of the above reasons (and others), the people selling various fMRI-related services–e.g., “neuromarketing” firms that purport to tell major companies how people “really” feel about their brands–are basically selling snake oil.

Anyway, it’s a good piece, so give it a read. Poldrack is widely respected in the field of cognitive neuroscience for his thoughtfulness and methodological rigor, so it’s always worth paying attention to what he has to say on such matters.

[hat-tip: MindHacks]

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).

The limitations of fMRI are not related to physics or poor engineering, and are unlikely to be resolved by increasing the sophistication and power of the scanners; they are instead due to the circuitry and functional organization of the brain, as well as to inappropriate experimental protocols that ignore this organization.

That’s not to say that all is lost, of course. On the whole, Logothetis is pretty optimistic about the value of fMRI, even going so far as to suggest that “MRI is currently the best tool we have for gaining insights into brain function and formulating interesting and eventually testable hypotheses”; it’s just that it’s not perfect by a long shot.  But anyway, there’s much more to the review than I can convey coherently in my current sleepy state, so if you have access to Nature, it’s definitely worth reading.

The Science piece (“Growing Pains for fMRI”) is a much lighter news article by Greg Miller, and it focuses mostly on a controversy that played out in the pages of the New York Times last year. The thumbnail sketch is  that one group of fMRI researchers did some very shoddy “research” on the way people view the different election candidates, and another (larger) group of researchers called them on it.  The exchange then led to a period of widespread soul-searching amongst cognitive neuroscientists, until ultimately, in March 2008, the Cognitive Neuroscience Society imposed a moratorium on publication of all fMRI data until a common set of guidelines for rigorous and ethical research conduct was agreed upon.  Ok, that last part is completely made up. But the point is that the article is a good read, and you should check it out if you can.  It’s not often you hear one scientist say that another scientist’s study was “really closer to astrology than it was to real science” (for the record, I agree with that assessment in this case).