A brave new default mode in meditation practitioners- or just confused controls? Review of Brewer (2011)

Given that my own work focuses on cognitive control, intrinsic connectivity, and mental-training (e.g. meditation) I was pretty excited to see Brewer et al’s paper on just these topics appear in PNAS just in time for the winter holidays. I meant to review it straight away but have been buried under my own data analysis until recently. Sadly, when I finally got around to delving into it, my overall reaction was lukewarm at best. Without further ado, my review of:

“Meditation experience is associated with differences in default mode network activity and connectivity

Abstract:

“Many philosophical and contemplative traditions teach that “living in the moment” increases happiness. However, the default mode of humans appears to be that of mind-wandering, which correlates with unhappiness, and with activation in a network of brain areas associated with self-referential processing. We investigated brain activity in experienced meditators and matched meditation-naive controls as they performed several different meditations (Concentration, Loving-Kindness, Choiceless Awareness). We found that the main nodes of the default mode network(medial prefrontal and posterior cingulate cortices) were relatively deactivated in experienced meditators across all meditation types. Furthermore, functional connectivity analysis revealed stronger coupling in experienced meditators between the posterior cingulate, dorsal anterior cingulate, and dorsolateral prefrontal cortices (regions previously implicated in self- monitoring and cognitive control), both at baseline and during meditation. Our findings demonstrate differences in the default-mode network that are consistent with decreased mind-wandering. As such, these provide a unique understanding of possible neural mechanisms of meditation.”

Summary:

Aims: 9/10

Methods: 5/10

Interpretation: 7/10

Importance/Generalizability: 4/10

Overall: 6.25/10

The good: simple, clear cut design, low amount of voodoo, relatively sensible findings

The bad: lack of behavioral co-variates to explain neural data, yet another cross-sectional design

The ugly: prominent reporting of uncorrected findings, comparison of meditation-naive controls to practitioners using meditation instructions (failure to control task demands).

Take-home: Some interesting conclusions, from a somewhat tired and inconclusive design. Poor construction of baseline condition leads to a shot-gun spattering of brain regions with a few that seem interesting given prior work. Let’s move beyond poorly controlled cross-sections and start unravelling the core mechanisms (if any) involved in mindfulness.

Extended Review:
Although this paper used typical GLM and functional connectivity analyses, it loses points in several areas. First, although the authors repeatedly suggest that their “relative paucity of findings” may be “driven by the sensitivity of GLM analysis to fluctuations at baseline… and since meditation practitioners may be (meditating) at baseline…” the contrast would be weak. However, I will side with Jensen et al (2011) here in saying: Meditation naive controls receiving less than 5 minutes of instruction in “focused attention, loving-kindness and choiceless awareness” are simply no controls at all. The argument that the inability of the GLM to detect differences that are quite obviously confounded by a lack of an appropriately controlled baseline is galling at best. This is why we use a GLM-approach; it’s senseless to make conclusions about brain activity when your baseline is no baseline at all. Telling meditation-naive controls to utilize esoteric cultural practices of which they have only just been introduced too, and then comparing that to highly experienced practitioners is a perfect storm of cognitive confusion and poorly controlled demand characteristic. Further, I am disappointed in the review process that allowed the following statement “We found a similar pattern in the medial prefrontal cortex (mPFC), another primary node of the DMN, although it did not survive whole-brain correction for signifigance” followed by this image:

image

These results are then referred to repeatedly in the following discussion. I’m sorry, but when did uncorrected findings suddenly become interpretable? I blame the reviewers here over the authors- they should have known better. The MPFC did not survive correction and hence should not be included in anything other than a explicitly stated as such “exploratory analysis”. In fact it’s totally unclear from the methods section of this paper how these findings where at all discovered: did the authors first examine the uncorrected maps and then re-analyze them using the FWE correction? Or did they reduce their threshold in an exploratory post-hoc fashion? These things make a difference and I’m appalled that the reviewers let the article go to print as it is, when figure 1 and the discussion clearly give the non-fMRI savy reader the impression that a main finding of this study is MPFC activation during meditation. Can we please all agree to stop reporting uncorrected p-values?

I will give the authors this much; the descriptions of practice, and the theoretical guideposts are all quite coherent and well put-together. I found their discussion of possible mechanisms of DMN alteration in meditation to be intriguing, even if I do not agree with their conclusion. Still, it pains me to see a paper with so much potential fail to address the pitfalls in meditation research that should now be well known. Indeed the authors themselves make much ado about how difficult proper controls are, yet seem somehow oblivious to the poorly controlled design they here report. This leads me to my own reinterpretation of their data.

A new default mode, or confused controls?

Brewer et al (2011) report that, when using a verbally guided meditation instruction with meditation naive-controls and experienced practitioners, greater activations in PCC, temporal regions, and for loving-kindness, amygdala are found. Given strong evidence by colleagues Christian Jensen et al (2011) that these kinds of contrasts better represent differences in attentional effort than any mechanism inherent to meditation, I can’t help but wonder if what were seeing here is simply some controls trying to follow esoteric instructions and getting confused in the process. Consider the instruction for the choiceless awareness condition:

“Please pay attention to whatever comes into your awareness, whether it is a thought, emotion, or body sensation. Just follow it until something else comes into your awareness, not trying to hold onto it or change it in any way. When something else comes into your awareness, just pay attention to it until the next thing comes along”

Given that in most contemplative traditions, choiceless awareness techniques are typically late-level advanced practices, in which the very concept of grasping to a stimulus is distinctly altered and laden with an often spiritual meaning, it seems obvious to me that such an instruction constitutes and excellent mindwandering inducement for naive-controls. Do you meditate? I do a little, and yet I find these instructions extremely difficult to follow without essentially sending my mind in a thousand directions. Am I doing this correctly?  When should I shift? Is this a thought or am I just feeling hungry? These things constitute mind-wandering but for the controls, I would argue they constitute following the instructions. The point is that you simply can’t make meaningful conclusions about the neural mechanisms involved in mindfulness from these kinds of instructions.

Finally, let’s examine the functional-connectivity analysis. To be honest, there isn’t a whole lot to report here; the functional connectivity during meditation is perhaps confounded by the same issues I list above, which seems to me a probable cause for the diverse spread of regions reported between controls and meditators. I did find this bit to be interesting:

“Using the mPFC as the seed region, we found increased connectivity with the fusiform gyrus, inferior temporal and parahippocampal gyri, and left posterior insula (among other regions) in meditators relative to controls during meditation (Fig. 3, Fig. S1H, and Table S3). A subset of those regions showed the same relatively increased connectivity in meditators during the baseline period as well (Fig. S1G and Table1)

I found it interesting that the meditation conditions appear to co-activate MPFC and insula, and would love to see this finding replicated in properly controlled design. I also have a nagging wonder as to why the authors didn’t bother to conduct a second-level covariance analysis of their findings with the self-reported mind-wandering scores. If these findings accurately reflect meditation-induced alterations in the DMN, or as the authors more brazenly suggest “a entirely new default network”, wouldn’t we expect their PCC modulations to be predicted by individual variability in mind-wandering self-reports? Of course, we could open the whole can of worms that is “what does it mean when you ask participants if they ‘experienced mind wandering” but I’ll leave that for a future review. At least the authors throw a bone to neurophenomenology, suggesting in the discussion that future work utilize first-person methodology. Indeed.

Last, it occurs to me that the primary finding, of increased DLPFC and ACC in meditation>Controls, also fits well with my intepretation that this design is confounded by demand characteristics. If you take a naive subject and put them in the scanner with these instructions, I’ve argued that their probably going to do something a whole lot like mind-wandering. On the other hand, an experienced practitioner has a whole lot of implicit pressure on them to live up to their tradition. They know what they are their for, and hence they know that they should be doing their thing with as much effort as possible. So what does the contrast meditation>naive really give us? It gives us mind-wandering in the naive group, and increased attentional effort in the practitioner group. We can’t conclude anything from this design regarding mechanisms intrinsic to mindfulness; I predict that if you constructed a similar setting with any kind of dedicated specialist, and gave instructions like “think about your profession, what it means to you, remember a time you did really well” you would see the exact same kind of results. You just can’t compare the uncomparable.

Disclaimer: as usual, I review in the name of science, and thank the authors whole-heartily for the great effort and attention to detail that goes into these projects.  Also it’s worth mentioning that my own research focuses on many of these exact issues in mental training research, and hence i’m probably a bit biased in what I view as important issues.

6 thoughts on “A brave new default mode in meditation practitioners- or just confused controls? Review of Brewer (2011)

  1. Thanks for the thoughtful review, Micah. I’ve always felt uneasy about what meditation naive subjects actually do when asked to meditate. I can’t envision what a proper meditation state control would be, so I’m just going to stick to trait changes in my own work for the time being.

    It’s really too bad they got away with that figure and discussion of the uncorrected mPFC result…

    • Thanks Michael. I can’t believe top journals like PNAS are letting these kinds of results get through. It really only serves to weaken the credibility of an otherwise not-so-bad paper, and greatly lessens the journal in my opinion. With PNAS’s lax publishing style, I’m sure a great many lay neuroscientists in other fields read their articles. It’s a great way to cause a lot of confusion.

      I think the question about baseline is really interesting. We’ve all had to struggle with it at one point or another in our contemplative research. In my studies I’ve typically attempted to circumvent the issue but not using meditation as an independent variable. By using classical cognitive paradigms and triangulating from different forms of data (1st person, fmri, behavioral, physiological) I hope to find insight into both the mechanisms of meditation and their transfer effects.

      Still, I think the kind of research attempted in Brewer is worthwhile, we just have to think a bit more carefully about how to construct our control. In my last study, we used a blinded, financially motivated experimental set-up. Our controls had no idea that they were in a meditation study; they thought they where in a study on individual differences in attention, competing for a sizable cash reward.

      Of course you can’t do this with actual meditation states. This makes me think the only real way to study them is through repeated measures design.

  2. I’m glad to see that our recent work is of interest, and welcome constructive criticism to help us improve the science. Just a few clarifying points and questions:

    Regarding the choiceless awareness, Micah brings up an interesting point about it being taught “as and advanced technique.” Often, depending on the teacher and tradition, choiceless awareness is taught after some type of stabilizing concentration practice. However, in the influential Mahasi Sayadaw “noting practice” in which everything is fair game for attention, it is taught right from the getgo. And perhaps partly because of its simplicity, it is quite a powerful technique. Additionally, as Micah ponders: “it seems obvious to me that such an instruction constitutes and excellent mindwandering inducement for naive-controls.” Yes, one would think that this would be the case. And if so, one would also expect novices to INCREASE their PCC activity (which has been shown by many groups previously) rather than decrease it. We were quite surprised to see that in this condition particularly, novices actually decreased PCC activation relative to the resting-state baseline, enough in fact, that we didn’t see any between group differences in this condition. This can be seen in figure 1. This was an interesting surprise to me, and warrants following up: perhaps novices when given these seemingly difficult instructions are able to put them into practice to some degree.

    Also, perhaps I missed something, but was a little confused by the comment: “To be honest, there isn‚t a whole lot to report here; the functional connectivity during meditation is perhaps confounded by the same issues I list above, which seems to me a probable cause for the diverse spread of regions reported between controls and meditators.” How exactly is functional connectivity confounded by a baseline condition, when it is measured 1) without using a contrast condition (by definition, it doesn’t use one), and 2) when it is measured at baseline itself?. I agree that meditators might be inducing different connectivity patterns during meditation, which as I’ll point out below may still be interesting itself and not just a confound of confused controls. However, what was particularly interesting, and very surprising, was that when meditators were told to “lie still and not do anything in particular” (which is the standard instruction for measuring resting-state connectivity), they showed the same pattern of connectivity that they did during meditation. Yes, perhaps they are paying attention at baseline when they aren’t doing anything in particular, but this is great! Isn’t that what meditators aspire to?

    Moreover, as Micah points out: “Last, it occurs to me that the primary finding, of increased DLPFC and ACC in meditation>Controls, also fits well with my intepretation that this design is confounded by demand characteristics. If you take a naive subject and put them in the scanner with these instructions, I‚ve argued that their probably going to do something a whole lot like mind-wandering.” And you and many others have argued this well! Yes, this is how Marc Raichle’s group discovered the DMN, and an entire field was born. And our data support this, as controls report significantly more mind-wandering than meditators. But how does this explain the altered connectivity findings? I would refer any interested reader to papers that highlight an ANTI-correlation between the ACC, dlPFC and PCC, which have has replicated enough that these two networks are dubbed the “task positive” (ACC and dlPFC among others) and “task negative” (DMN) networks respectively (See FOX PNAS 2005, Fransson 2005, Castellanos 2008 among others). So, why do these two, normally anti-correlated networks, actually link up in meditators both during meditation and at baseline? If this were the case in the the experiment that Micah hypothesizes, it would have already been seen by a number of groups previously (and we likely wouldn’t have even thought to submit our work to PNAS). I’d welcome any explanation of this that I may have missed. As things stand, it seems to me that this indeed indicates perhaps if not a brave, at least a “new default mode” in meditators. I agree that prospective studies are needed to confirm these findings.

    Finally, I’d also suggest that 1) if you, Micah feel strongly about these critiques, that you write a letter to PNAS, such that this type of discussion happen in an open, and balanced forum, as most journals publish both letters and replies from authors. My sense of science at its best is one of open and curious observation. I would also encourage neuroscience.com to invite replies by authors, such that its forum may support a more collaborative and balanced discussion.

    Sincerely, Judson Brewer

    • Hi Judson,

      First of all, thanks for your comment- it’s great to hear back from the author, something I rarely expect when writing these reviews. I like your idea of inviting authors to comment on my reviews (I think that’s what you meant, it’s a bit late here in Denmark). To be honest, given that this blog merely represents the musings of a scientist in training, I’m not sure i’d give myself enough credit to imagine that the authors would want to comment! But I am very grateful when it does happen.

      So, let me try and address your concerns. First, on the comment about choiceless awareness, I do admit to picking on you a bit as of the three meditation instructions that one is clearly the most confusing for controls. However I’d be very cautious to interpret the internal teachings of a tradition like the one you mention as a basis for making predictions about how typical controls perform. In my own experience with contemplative practice, and in my longitudinal study, there is a great deal of individual difference in how these things are perceived by naive-controls.

      I’ve run Norman Farb’s (2009) paradigm for example, and I must say that in running it, I went from believing the result to being very skeptical. For every one control who seemed to get the basic idea quickly (and this was very simple instructions about “judging” or “sensing” one’s reaction to trait-adjectives) there would be another who seemed to think I was crazy. We shouldn’t take for granted the way our cultural background with these practices can blind us to just how confusing they may be. I know if I think back to my first exposure to meditation instruction, it was anything but enlightening.

      But this is all speculation; all we can really see from figure 1 is that there doesn’t seem to be a significant effect of meditation in the controls. Was the within-group negative signal change for choiceless awareness significant? If we make the simple case that rest = mindwandering, and more DMN = more mind-wandering, than a null effect would imply that controls are mind wandering at both baseline and meditation, no? I would also be careful to interpret increased PCC activity in such a straight-forward manner- see Raichle (2010) for arguments that construing DMN as conscious mind-wandering may be ill advised.

      As for the bit about functionally connectivity, I’m afraid it was my shoddy writing. I’m aware that FC simply measures voxelwise correlation within a condition, not a contrast. What I was getting at is that, your FC pattern suggests greater DMN-central executive (CEN) connectivity for meditation > control. If your controls “meditation” is really just more mind-wandering, and the practitioners are in a focused state of meditation, it’s not really surprising that they’d show greater recruitment of CEN areas. The point is that, if one group is focusing on something (meditation), and the other group is mind-wandering, your independent variable is attentional effort, not meditation.

      I’m a big fan of the anti-correlation hypothesis, but we have to keep in mind that true anti-correlation at rest is controversial. Murphy (2009) demonstrated quite strongly that anti-correlations are mathematically induced by global-mean regression. I have a little matlab script that induces anti-correlations to perfectly correlated timeseries when you remove the global mean. I know you didn’t run a GMR, but my point is just that we need to resist this kind of reverse-inference, particularly with a region like the PCC. I’ve spent a fair amount of time trying to convince folks like Chris Frith and Torben Lund that the MPFC is most likely anti-correlated to the CEN, depending on the nature of the task. But this isn’t clear at all for regions like the PCC that have extremely complex connectivity and a not at all linear relationship to cognitive control and task demands.

      Anyway, I hope this clears my thoughts up a bit. It’s almost 1AM here, so perhaps not. I think I should stress that my frustration was with PNAS for letting the uncorrected MPFC figure slide. It really creates the impression that the MPFC was significantly de-activated, when in reality we’re probably dealing with a false positive. I’d love it if they didn’t make me go digging around in the SI to see what exactly transpired in an experiment, but i’m not holding my breath on that one. Thanks for your comment, and for the paper! I would like to add that I do find your results interesting, and they certainly have already been helpful in interpreting my own findings. I can’t really complain if a high-impact journal like PNAS is still publishing cross-sectional findings in this area. I think we can all agree that there are serious confounds in any design that compares naive controls and advanced practitioners without in someway manipulating demand characteristics. While my own data is full of it’s own flaws (oh god, the flaws are deep…) I’m excited to think it may be one of the first fMRI studies to use a fully active control- maybe i’ll consider a submission to PNAS rather than a nasty letter. Getting accepted there would definitely go lengths to convince my Danish colleagues that there isn’t some kind of St.Louis conspiracy on the editorial board😉

      Best,
      Micah

      P.S. Very curious to hear what you make of my post on respiratory artifacts in mACC, insula, and MPFC. Do you think your practitioners could have been breathing at different rates during the baseline condition?

Leave a Reply

Fill in your details below or click an icon to log in:

WordPress.com Logo

You are commenting using your WordPress.com account. Log Out / Change )

Twitter picture

You are commenting using your Twitter account. Log Out / Change )

Facebook photo

You are commenting using your Facebook account. Log Out / Change )

Google+ photo

You are commenting using your Google+ account. Log Out / Change )

Connecting to %s