Or so i’m going to claim because science is basically about making up whatever qualitative opinion you like and hard-selling it to a high impact journal right? Last night a paper appeared in PNAS early access entitled “Nature experience reduces rumination and subgenual prefrontal cortex activation” as a contributed submission. Like many of you I immediately felt my neurocringe brain area explode with activity as I began to smell the sickly sweet scent of gimmickry. Now I don’t have a lot of time so I was worried I wouldn’t be able to cover this paper in any detail. But never to worry, because the entire paper is literally two ANOVAs!
The paper begins with a lofty appeal to our naturalistic sensibilities; we’re increasingly living in urban areas, this trend is associated with poor mental health outcomes, and by golly-gee, shouldn’t we have a look at the brain to figure this all out? The authors set about testing their hypothesis by sending 19 people out into the remote wilderness of the Stanford University campus, or an urban setting:
The nature walk took place in a greenspace near Stanford University spanning an area ∼60 m northwest of Junipero Serra Boulevard and extending away from the street in a 5.3-km loop, including a significant stretch that is far (>1 km) from the sounds and sights of the surrounding residential area. As one proxy for urbanicity, we measured the proportion of impervious surface (e.g., asphalt, buildings, sidewalks) within 50 m of the center of the walking path (Fig. S4). Ten percent of the area within 50 m of the center of the path comprised of impervious surface (primarily of the asphalt path). Cumulative elevation gain of this walk was 155 m. The natural environment of the greenspace comprises open California grassland with scattered oaks and native shrubs, abundant birds, and occasional mammals (ground squirrels and deer). Views include neighboring, scenic hills, and distant views of the San Francisco Bay, and the southern portion of the Bay Area (including Palo Alto and Mountain View to the south, and Menlo Park and Atherton to the north). No automobiles, bicycles, or dogs are permitted on the path through the greenspace.
Wow, where can I sign up for this truly Kerouac-inspired bliss? The control group on the other hand had to survive the horrors of the palo-alto urban wasteland:
The urban walk took place on the busiest thoroughfare in nearby Palo Alto (El Camino Real), a street with three to four lanes in each direction and a steady stream of traffic. Participants were instructed to walk down one side of the street in a southeasterly direction for 2.65 km, before turning around at a specific point marked on a map. This spot was chosen as the midpoint of the walk for the urban walk to match the nature walk with respect to total distance and exercise. Participants were instructed to cross the street at a pedestrian crosswalk/stoplight, and return on the other side of the street (to simulate the loop component of the nature walk and greatly reduce repeated encounters with the same environmental stimuli on the return portion of the walk), for a total distance of 5.3 km; 76% of the area within 50mof the center of this section of El Camino was comprised of impervious surfaces (of roads and buildings) (Fig. S4). Cumulative elevation gain of this walk was 4 m. This stretch of road consists of a significant amount of noise from passing cars. Buildings are almost entirely single- to double-story units, primarily businesses (fast food establishments, cell phone stores, motels, etc.). Participants were instructed to remain on the sidewalk bordering the busy street and not to enter any buildings. Although this was the most urban area we could select for a walk that was a similar distance from the MRI facility as the nature walk, scattered trees were present on both sides of El Camino Real. Thus, our effects may represent a conservative estimate of effects of nature experience, as our urban group’s experience was not devoid of natural elements.
And they got that approved by the local ethics board? The horror!
The authors gave both groups a self-reported rumination questionnaire before and after the walk, and also acquired some arterial spin labeling MRIs. Here is where the real fun gets started – and basically ends – as the paper is almost entirely comprised of group by time ANOVAs on these two measures. I wish I could say I was suprised by what I found in the results:
That’s right folks – the key behavioral interaction of the paper – is non-significant. Measly. Minuscule. Forget about p-values for a second and consider the gall it takes to not only completely skim over this fact (nowhere in the paper is it mentioned) and head right to the delicious t-tests, but to egregiously promote this ‘finding’ in the title, abstract, and discussion as showing evidence for an effect of nature on rumination! Erroneous interaction for the win, at least with PNAS contributed submissions right?! The authors also analyzed the brain data in the same way – this time actually sticking with their NHST – and find that some brain area that has been previously related to some bad stuff showed reduced activity. And that – besides a heart rate and respiration control analyses – is it. No correlations with the (non-significant) behavior. Just pure and simple reverse inference piled on top of fallacious interpretation of a non-significant interaction. Never-mind the wonky and poorly operationalized research question!
See folks, high impact science is easy! Just have friends in the National Academy…
I’ll leave you with this gem from the methods:
“‘One participant was eliminated in analysis of self-reported rumination due to a decrease in rumination after nature experience that was 3 SDs below the mean.'”
That dude REALLY got his time’s worth from the walk. Or did the researchers maybe forget to check if anyone smoked a joint during their nature walk?
Over the past 5 years, resting-state fMRI (rsfMRI) has exploded in popularity. Literally dozens of papers are published each day examining slow (< .1 hz) or “low frequency” fluctuations in the BOLD signal. When I first moved to Europe I was caught up in the somewhat North American frenzy of resting state networks. I couldn’t understand why my Danish colleagues, who specialize in modelling physiological noise in fMRI, simply did not take the literature seriously. The problem is essentially that the low frequencies examined in these studies are the same as those that dominate physiological rhythms. Respiration and cardiac pulsation can make up a massive amount of variability in the BOLD signal. Before resting state fMRI came along, nearly every fMRI study discarded any data frequencies lower than one oscillation every 120 seconds (e.g. 1/120 Hz high pass filtering). Simple things like breath holding and pulsatile motion in vasculature can cause huge effects in BOLD data, and it just so happens that these artifacts (which are non-neural in origin) tend to pool around some of our favorite “default” areas: medial prefrontal cortex, insula, and other large gyri near draining veins.
Naturally this leads us to ask if the “resting state networks” (RSNs) observed in such studies are actually neural in origin, or if they are simply the result of variations in breath pattern or the like. Obviously we can’t answer this question with fMRI alone. We can apply something like independent component analysis (ICA) and hope that it removes most of the noise- but we’ll never really be 100% sure we’ve gotten it all that way. We can measure the noise directly (e.g. “nuisance covariance regression”) and include it in our GLM- but much of the noise is likely to be highly correlated with the signal we want to observe. What we need are cross-modality validations that low-frequency oscillations do exist, that they drive observed BOLD fluctuations, and that these relationships hold even when controlling for non-neural signals. Some of this is already established- for example direct intracranial recordings do find slow oscillations in animal models. In MEG and EEG, it is well established that slow fluctuations exist and have a functional role.
So far so good. But what about in fMRI? Can we measure meaningful signal while controlling for these factors? This is currently a topic of intense research interest. Marcus Raichle, the ‘father’ of the default mode network, highlights fascinating multi-modal work from a Finnish group showing that slow fluctuations in behavior and EEG signal coincide (Raichle and Snyder 2007; Monto, Palva et al. 2008). However, we should still be cautious- I recently spoke to a post-doc from the Helsinki group about the original paper, and he stressed that slow EEG is just as contaminated by physiological artifacts as fMRI. Except that the problem is even worse, because in EEG the artifacts may be several orders of magnitude larger than the signal of interest[i].
Understandably I was interested to see a paper entitled “Correlated slow fluctuations in respiration, EEG, and BOLD fMRI” appear in Neuroimage today (Yuan, Zotev et al. 2013). The authors simultaneously collected EEG, respiration, pulse, and resting fMRI data in 9 subjects, and then perform cross-correlation and GLM analyses on the relationship of these variables, during both eyes closed and eyes open rest. They calculate Respiratory Volume per Time (RVT), a measure developed by Rasmus Birn, to assign a respiratory phase to each TR (Birn, Diamond et al. 2006). One key finding is that the global variations in EEG power are strongly predicted by RVT during eyes closed rest, with a maximum peak correlation coefficient of .40. Here are the two time series:
You can clearly see that there is a strong relationship between global alpha (GFP) and respiration (RVT). The authors state that “GFP appears to lead RVT” though I am not so sure. Regardless, there is a clear relationship between eyes closed ‘alpha’ and respiration. Interestingly they find that correlations between RVT and GFP with eyes open were not significantly different from chance, and that pulse did not correlate with GFP. They then conduct GLM analyses with RVT and GFP as BOLD regressors. Here is what their example subject looked like during eyes-closed rest:
Notice any familiar “RSNs” in the RVT map? I see anti-correlated executive deactivation and default mode activation! Very canonical. Too bad they are breath related. This is why noise regression experts tend to dislike rsfMRI, particularly when you don’t measure the noise. We also shouldn’t be too surprised that the GFP-BOLD and RVT-BOLD maps look similar, considering that GFP and RVT are highly correlated. After looking at these correlations separately, Yuan et al perform RETROICOR physiological noise correction and then reexamine the contrasts. Here are the group maps:
Things look a bit less default-mode-like in the group RVT map, but the RVT and GFP maps are still clearly quite similar. In panel D you can see that physiological noise correction has a large global impact on GFP-BOLD correlations, suggesting that quite a bit of this co-variance is driven by physiological noise. Put simply, respiration is explaining a large degree of alpha-BOLD correlation; any experiment not modelling this covariance is likely to produce strongly contaminated results. Yuan et al go on to examine eyes-open rest and show that, similar to their RVT-GFP cross-correlation analysis, not nearly as much seems to be happening in eyes open compared to closed:
The authors conclude that “In particular, this correlation between alpha EEG and respiration is much stronger in eyes-closed resting than in eyes-open resting” and that “[the] results also suggest that eyes-open resting may be a more favorable condition to conduct brain resting state fMRI and for functional connectivity analysis because of the suppressed correlation between low-frequency respiratory fluctuation and global alpha EEG power, therefore the low-frequency physiological noise predominantly of non-neuronal origin can be more safely removed.” Fair enough- one conclusion is certainly that eyes closed rest seems much more correlated with respiration than eyes open. This is a decent and useful result of the study. But then they go on to make this really strange statement, which appears in the abstract, introduction, and discussion:
“In addition, similar spatial patterns were observed between the correlation maps of BOLD with global alpha EEG power and respiration. Removal of respiration related physiological noise in the BOLD signal reduces the correlation between alpha EEG power and spontaneous BOLD signals measured at eyes-closed resting. These results suggest a mutual link of neuronal origin between the alpha EEG power, respiration, and BOLD signals”’ (emphasis added)
That’s one way to put it! The logic here is that since alpha = neural activity, and respiration correlates with alpha, then alpha must be the neural correlate of respiration. I’m sorry guys, you did a decent experiment, but I’m afraid you’ve gotten this one wrong. There is absolutely nothing that implies alpha power cannot also be contaminated by respiration-related physiological noise. In fact it is exactly the opposite- in the low frequencies observed by Yuan et al the EEG data is particularly likely to be contaminated by physiological artifacts! And that is precisely what the paper shows – in the author’s own words: “impressively strong correlations between global alpha and respiration”. This is further corroborated by the strong similarity between the RVT-BOLD and alpha-BOLD maps, and the fact that removing respiratory and pulse variancedrastically alters the alpha-BOLD correlations!
So what should we take away from this study? It is of course inconclusive- there are several aspects of the methodology that are puzzling to me, and sadly the study is rather under-powered at n = 9. I found it quite curious that in each of the BOLD-alpha maps there seemed to be a significant artifact in the lateral and posterior ventricles, even after physiological noise correction (check out figure 2b, an almost perfect ventricle map). If their global alpha signal is specific to a neural origin, why does this artifact remain even after physiological noise correction? I can’t quite put my finger on it, but it seems likely to me that some source of noise remained even after correction- perhaps a reader with more experience in EEG-fMRI methods can comment. For one thing their EEG motion correction seems a bit suspect, as they simply drop outlier timepoints. One way or another, I believe we should take one clear message away from this study – low frequency signals are not easily untangled from physiological noise, even in electrophysiology. This isn’t a damnation of all resting state research- rather it is a clear sign that we need be to measuring these signals to retain a degree of control over our data, particularly when we have the least control at all.
Birn, R. M., J. B. Diamond, et al. (2006). “Separating respiratory-variation-related fluctuations from neuronal-activity-related fluctuations in fMRI.” Neuroimage31(4): 1536-1548.
Monto, S., S. Palva, et al. (2008). “Very slow EEG fluctuations predict the dynamics of stimulus detection and oscillation amplitudes in humans.” The Journal of Neuroscience28(33): 8268-8272.
Raichle, M. E. and A. Z. Snyder (2007). “A default mode of brain function: a brief history of an evolving idea.” Neuroimage37(4): 1083-1090.
Yuan, H., V. Zotev, et al. (2013). “Correlated Slow Fluctuations in Respiration, EEG, and BOLD fMRI.” NeuroImage pp. 1053-8119.
[i] Note that this is not meant to be in anyway a comprehensive review. A quick literature search suggests that there are quite a few recent papers on resting BOLD EEG. I recall a well done paper by a group at the Max Planck Institute that did include noise regressors, and found unique slow BOLD-EEG relations. I cannot seem to find it at the moment however!
Here in the science blog-o-sphere we often like to run to the presses whenever a laughably bad study comes along, pointing out all the incredible feats of ignorance and sloth. However, this can lead to science-sucks cynicism syndrome (a common ailment amongst graduate students), where one begins to feel a bit like all the literature is rubbish and it just isn’t worth your time to try and do something truly proper and interesting. If you are lucky, it is at this moment that a truly excellent paper will come along at the just right time to pick up your spirits and re-invigorate your work. Today I found myself at one such low-point, struggling to figure out why my data suck, when just such a beauty of a paper appeared in my RSS reader.
The paper, “Brief body-scan meditation practice improves somatosensory perceptual decision making”, appeared in this month’s issue of Consciousness and Cognition. Laura Mirams et al set out to answer a very simple question regarding the impact of meditation training (MT) on a “somatic signal detection task” (SSDT). The study is well designed; after randomization, both groups received audio CDs with 15 minutes of daily body-scan meditation or excerpts from The Lord of The Rings. For the SSD task, participants simply report when they felt a vibration stimulus on the finger, where the baseline vibration intensity is first individually calibrated to a 50% detection rate. The authors then apply a signal-detection analysis framework to discern the sensitivity or d’ and decision criteria c.
Mirams et al found that, even when controlling for a host of baseline factors including trait mindfulness and baseline somatic attention, MT led to a greater increase in d’ driven by significantly reduced false-alarms. Although many theorists and practitioners of MT suggest a key role for interoceptive & somatic attention in related alterations of health, brain, and behavior, there exists almost no data addressing this prediction, making these findings extremely interesting. The idea that MT should impact interoception and somatosensation is very sensible- in most (novice) meditation practices it is common to focus attention to bodily sensations of, for example, the breath entering the nostril. Further, MT involves a particular kind of open, non-judgemental awareness of bodily sensations, and in general is often described to novice students as strengthening the relationship between the mind and sensations of the body. However, most existing studies on MT investigate traditional exteroceptive, top-down elements of attention such as conflict resolution and the ability to maintain attention fixation for long periods of time.
While MT certainly does involve these features, it is arguable that the interoceptive elements are more specific to the precise mechanisms of interest (they are what you actually train), whereas the attentional benefits may be more of a kind of side effect, reflecting an early emphasis in MT on establishing attention. Thus in a traditional meditation class, you might first learn some techniques to fixate your attention, and then later learn to deploy your attention to specific bodily targets (i.e. the breath) in a particular way (non-judgmentally). The goal is not necessarily to develop a super-human ability to filter distractions, but rather to change the way in which interoceptive responses to the world (i.e. emotional reactions) are perceived and responded to. This hypothesis is well reflected in the elegant study by Mirams et al; they postulate specifically that MT will lead to greater sensitivity (d’), driven by reduced false alarms rather than an increased hit-rate, reflecting a greater ability to discriminate the nature of an interoceptive signal from noise (note: see comments for clarification on this point by Steve Fleming – there is some ambiguity in interpreting the informational role of HR and FA in d’). This hypothesis not only reflects the theoretically specific contribution of MT (beyond attention training, which might be better trained by video games for example), but also postulates a mechanistically specific hypothesis to test this idea, namely that MT leads to a shift specifically in the quality of interoceptive signal processing, rather than raw attentional control.
At this point, you might ask if everyone is so sure that MT involves training interoception, why is there so little data on the topic? The authors do a great job reviewing findings (even including currently in-press papers) on interoception and MT. Currently there is one major null finding using the canonical heartbeat detection task, where advanced practitioners self-reported improved heart beat detection but in reality performed at chance. Those authors speculated that the heartbeat task might not accurately reflect the modality of interoception engaged in by practitioners. In addition a recent study investigated somatic discrimination thresholds in a cross-section of advanced practitioners and found that the ability to make meta-cognitive assessments of ones’ threshold sensitivity correlated with years of practice. A third recent study showed greater tactile sensation acuity in practitioners of Tai Chi. One longitudinal study [PDF], a wait-list controlled fMRI investigation by Farb et al, found that a mindfulness-based stress reduction course altered BOLD responses during an attention-to-breath paradigm. Collectively these studies do suggest a role of MT in training interoception. However, as I have complained of endlessly, cross-sections cannot tell us anything about the underlying causality of the observed effects, and longitudinal studies must be active-controlled (not waitlisted) to discern mechanisms of action. Thus active-controlled longitudinal designs are desperately needed, both to determine the causality of a treatment on some observed effect, and to rule out confounds associated with motivation, demand-characteristic, and expectation. Without such a design, it is very difficult to conclude anything about the mechanisms of interest in an MT intervention.
In this regard, Mirams went above and beyond the call of duty as defined by the average paper. The choice of delivering the intervention via CD is excellent, as we can rule out instructor enthusiasm/ability confounds. Further the intervention chosen is extremely simple and well described; it is just a basic body-scan meditation without additional fluff or fanfare, lending to mechanistic specificity. Both groups were even instructed to close their eyes and sit when listening, balancing these often overlooked structural factors. In this sense, Mirams et al have controlled for instruction, motivation, intervention context, baseline trait mindfulness, and even isolated the variable of interest- only the MT group worked with interoception, though both exerted a prolonged period of sustained attention. Armed with these controls we can actually say that MT led to an alteration in interoceptive d’, through a mechanism dependent upon on the specific kind of interoceptive awareness trained in the intervention.
It is here that I have one minor nit-pick of the paper. Although the use of Lord of the Rings audiotapes is with precedent, and likely a great control for attention and motivation, you could be slightly worried that reading about Elves and Orcs is not an ideal control for listening to hours of tapes instructing you to focus on your bodily sensations, if the measure of interest involves fixating on the body. A pure active control might have been a book describing anatomy or body parts; then we could exhaustively conclude that not only is it interoception driving the findings, but the particular form of interoceptive attention deployed by meditation training. As it is, a conservative person might speculate that the observed differences reflect demand characteristics- MT participants deploy more attention to the body due to a kind of priming mechanism in the teaching. However this is an extreme nitpick and does not detract from the fact that Mirams and co-authors have made an extremely useful contribution to the literature. In the future it would be interesting to repeat the paradigm with a more body-oriented control, and perhaps also in advanced practitioners before and after an intensive retreat to see if the effect holds at later stages of training. Of course, given my interest in applying signal-detection theory to interoceptive meta-cognition, I also cannot help but wonder what the authors might have found if they’d applied a Fleming-style meta-d’ analysis to this study.
All in all, a clear study with tight methods, addressing a desperately under-developed research question, in an elegant fashion. The perfect motivation to return to my own mangled data ☺
First, let me apologize for an overlong hiatus from blogging. I submitted my PhD thesis October 1st, and it turns out that writing two papers and a thesis in the space of about three months can seriously burn out the old muse. I’ve coaxed her back through gentle offerings of chocolate, caffeine, and a bit of videogame binging. As long as I promise not to bring her within a mile of a dissertation, I believe we’re good for at least a few posts per month.
With that taken care of, I am very happy to report the successful publication of my first fMRI paper, published last month in the Journal of Neuroscience. The paper was truly a labor of love taking nearly 3 years to complete and countless hours of head-scratching work. In the end I am quite happy with the finished product, and I do believe my colleagues and I managed to produce a useful result for the field of mindfulness training and neuroplasticity.
note: this post ended up being quite long. if you are already familiar with mindfulness research, you may want to skip ahead!
First, depending on what brought you here, you may already be wondering why mindfulness is an interesting subject, particularly for a cognitive neuroscientist. In light of the large gaps regarding our understanding of the neurobiological foundations of neuroimaging, is it really the right time to apply these complex tools to meditation? Can we really learn anything about something as potentially ambiguous as “mindfulness”? Although we have a long way to go, and these are certainly fair questions, I do believe that the study of meditation has a lot to contribute to our understanding of cognition and plasticity.
Generally speaking, when you want to investigate some cognitive phenomena, a firm understanding of your target is essential to successful neuroimaging. Areas with years of behavioral research and concrete theoretical models make for excellent imaging subjects, as in these cases a researcher can hope to fall back on a sort of ‘ground truth’ to guide them through the neural data, which are notoriously ambiguous and difficult to interpret. Of course well-travelled roads also have their disadvantages, sometimes providing a misleading sense of security, or at least being a bit dry. While mindfulness research still has a ways to go, our understanding of these practices is rapidly evolving.
At this point it helps to stop and ask, what is meditation (and by extension, mindfulness)? The first thing to clarify is that there is no such thing as “meditation”- rather meditation is really term describing a family resemblance of highly varied practices, covering an array of both spiritual and secular practices. Meditation or “contemplative” practices have existed for more than a thousand years and are found in nearly every spiritual tradition. More recently, here in the west our unending fascination of the esoteric has lead to a popular rise in Yoga, Tai Chi, and other physically oriented contemplative practices, all of which incorporate an element of meditation.
At the simplest level of description [mindfulness] meditation is just a process of becoming aware, whether through actual sitting meditation, exercise, or daily rituals. Meditation (as a practice) was first popularized in the west during the rise of transcendental meditation (TM). As you can see in the figure below, interest in TM lead to an early boom in research articles. This boom was not to last, as it was gradually realized that much of this initially promising research was actually the product of zealous insiders, conducted with poor controls and in some cases outright data fabrication. As TM became known as a cult, meditation research underwent a dark age where publishing on the topic could seriously damage a research career. We can see also that around the 1990’s, this trend started to reverse as a new generation of researchers began investigating “mindfulness” meditation.
It’s easy to see from the above why when Jon Kabat-Zinn re-introduced meditation to the West, he relied heavily on the medical community to develop a totally secularized intervention-oriented version of meditation strategically called “mindfulness-based stress reduction.” The arrival of MBSR was closely related to the development of mindfulness-based cognitive therapy (MBCT), a revision of cognitive-behavioral therapy utilizing mindful practices and instruction for a variety of clinical applications. Mindfulness practice is typically described as involving at least two practices; focused attention (FA) and open monitoring (OM). FA can be described as simply noticing when attention wanders from a target (the breath, the body, or a flower for example) and gently redirecting it back to that target. OM is typically (but not always) trained at an later stage, building on the attentional skills developed in FA practice to gradually develop a sense of “non-judgmental open awareness”. While a great deal of work remains to be done, initial cognitive-behavioral and clinical research on mindfulness training (MT) has shown that these practices can improve the allocation of attentional resources, reduce physiological stress, and improve emotional well-being. In the clinic MT appears to effectively improve symptoms on a variety of pathological syndromes including anxiety and depression, at least as well as standard CBT or pharmacological treatments.
Has the quality of research on meditation improved since the dark days of TM? When answering this question it is important to note two things about the state of current mindfulness research. First, while it is true that many who research MT are also practitioners, the primary scholars are researchers who started in classical areas (emotion, clinical psychiatry, cognitive neuroscience) and gradually became involved in MT research. Further, most funding today for MT research comes not from shady religious institutions, but from well-established funding bodies such as the National Institute of Health and European Research Council. It is of course important to be aware of the impact prior beliefs can have on conducting impartial research, but with respect to today’s meditation and mindfulness researchers, I believe that most if not all of the work being done is honest, quality research.
However, it is true that much of the early MT research is flawed on several levels. Indeed several meta-analyses have concluded that generally speaking, studies of MT have often utilized poor design – in one major review only 8/22 studies met criteria for meta-analysis. The reason for this is quite simple- in the absence of pilot data, investigators had to begin somewhere. Typically it doesn’t bode well to jump into unexplored territory with an expensive, large sample, fully randomized design. There just isn’t enough to go off of- how would you know which kind of process to even measure? Accordingly, the large majority of mindfulness research to date has utilized small-scale, often sub-optimal experimental design, sacrificing experimental control in order build a basic idea of the cognitive landscape. While this exploratory research provides a needed foundation for generating likely hypotheses, it is also difficult to make any strong conclusions so long as methodological issues remain.
Indeed, most of what we know about these mindfulness and neuroplasticity comes from studies of either advanced practitioners (compared to controls) or “wait-list” control studies where controls receive no intervention. On the basis of the findings from these studies, we had some idea how to target our investigation, but there remained a nagging feeling of uncertainty. Just how much of the literature would actually replicate? Does mindfulness alter attention through mere expectation and motivation biases (i.e. placebo-like confounds), or can MT actually drive functionally relevant attentional and emotional neuroplasticity, even when controlling for these confounds?
The name of the game is active-control
Research to date links mindfulness practices to alterations in health and physiology, cognitive control, emotional regulation, responsiveness to pain, and a large array of positive clinical outcomes. However, the explicit nature of mindfulness training makes for some particularly difficult methodological issues. Group cross-sectional studies, where advanced practitioners are compared to age-matched controls, cannot provide causal evidence. Indeed, it is always possible that having a big fancy brain makes you more likely to spend many years meditating, and not that meditating gives you a big fancy brain. So training studies are essential to verifying the claim that mindfulness actually leads to interesting kinds of plasticity. However, unlike with a new drug study or computerized intervention, you cannot simply provide a sugar pill to the control group. Double-blind design is impossible; by definition subjects will know they are receiving mindfulness. To actually assess the impact of MT on neural activity and behavior, we need to compare to groups doing relatively equivalent things in similar experimental contexts. We need an active control.
There is already a well-established link between measurement outcome and experimental demands. What is perhaps less appreciated is that cognitive measures, particularly reaction time, are easily biased by phenomena like the Hawthorne effect, where the amount of attention participants receive directly contributes to experimental outcome. Wait-lists simply cannot overcome these difficulties. We know for example, that simply paying controls a moderate performance-based financial reward can erase attentional reaction-time differences. If you are repeatedly told you’re training attention, then come experiment time you are likely expect this to be true and try harder than someone who has received no such instruction. The same is true of emotional tasks; subjects told frequently they are training compassion are likely to spend more time fixating on emotional stimuli, leading to inflated self-reports and responses.
I’m sure you can quickly see how it is extremely important to control for these factors if we are to isolate and understand the mechanisms important for mindfulness training. One key solution is active-control, that is providing both groups (MT and control) with a “treatment” that is at least nominally as efficacious as the thing you are interested in. Active-control allows you exclude numerous factors from your outcome, potentially including the role of social support, expectation, and experimental demands. This is exactly what we set out to do in our study, where we recruited 60 meditation-naïve subjects, scanned them on an fMRI task, randomized them to either six weeks of MT or active-control, and then measured everything again. Further, to exclude confounds relating to social interaction, we came up with a particularly unique control activity- reading Emma together.
Jane Austen as Active Control – theory of mind vs interoception
To overcome these confounds, we constructed a specialized control intervention. As it was crucial that both groups believed in their training, we needed an instructor who could match the high level of enthusiasm and experience found in our meditation instructors. We were lucky to have the help of local scholar Mette Stineberg, who suggested a customized “shared reading” group to fit our purposes. Reading groups are a fun, attention demanding exercise, with purported benefits for stress and well-being. While these claims have not been explicitly tested, what mattered most was that Mette clearly believed in their efficacy- making for a perfect control instructor. Mette holds a PhD in literature, and we knew that her 10 years of experience participating in and leading these groups would help us to exclude instructor variables from our results.
With her help, we constructed a special condition where participants completed group readings of Jane Austin’s Emma. A sensible question to ask at this point is – “why Emma?” An essential element of active control is variable isolation, or balancing your groups in such way that, with the exception of your hypothesized “active ingredient”, the two interventions are extremely similar. As MT is thought to depend on a particular kind of non-judgmental, interoceptive kind of attention, Chris and Uta Frith suggested during an early meeting that Emma might be a perfect contrast. For those of you who haven’t read the novel, the plot is brimming over with judgment-heavy theory-of-mind-type exposition. Mette further helped to ensure a contrast with MT by emphasizing discussion sessions focused on character motives. In this way we were able to ensure that both groups met for the same amount of time each week, with equivalently talented and passionate instructors, and felt that they were working towards something worthwhile. Finally, we made sure to let every participant know at recruitment that they would receive one of two treatments intended to improve attention and well-being, and that any benefits would depend upon their commitment to the practice. To help them practice at home, we created 20-minute long CD’s for both groups, one with a guided meditation and the other with a chapter from Emma.
Unlike previous active-controlled studies that typically rely on relaxation training, reading groups depend upon a high level of social-interaction. Reading together allowed us not only to exclude treatment context and expectation from our results, but also more difficult effects of social support (the “making new friends” variable). To measure this, we built a small website for participants to make daily reports of their motivation and minutes practiced that day. As you can see in the figure below, when we averaged these reports we found that not only did the reading group practice significantly more than those in MT, but that they expressed equivalent levels of motivation to practice. Anecdotally we found that reading-group members expressed a high level of satisfaction with their class, with a sub-group of about 8 even continued their meetings after our study concluded. The meditation group by comparison, did not appear to form any lasting social relationships and did not continue meeting after the study. We were very happy with these results, which suggest that it is very unlikely our results could be explained by unbalanced motivation or expectation.
Impact of MT on attention and emotion
After we established that active control was successful, the first thing to look at was some of our outside-the-scanner behavioral results. As we were interested in the effect of meditation on both attention and meta-cognition, we used an “error-awareness task” (EAT) to examine improvement in these areas. The EAT (shown below) is a typical “go-no/go” task where subjects spend most of their time pressing a button. The difficult part comes whenever a “stop-trial” occurs and subject must quickly halt their response. In the case where the subject fails to stop, they then have the opportunity to “fix” the error by pressing a second button on the trial following the error. If you’ve ever taken this kind of task, you know that it can be frustratingly difficult to stop your finger in time – the response becomes quite habitual. Using the EAT we examined the impact of MT on both controlling responses (a variable called “stop accuracy”), as well as also on meta-cognitive self-monitoring (percent “error-awareness”).
We started by looking for significant group by time interactions on stop accuracy and error-awareness, which indicate that score fluctuation on a measure was statistically greater in the treatment (MT) group than in the control group. In repeated-measures design, this type of interaction is your first indication that the treatment may have had a greater effect than the control group. When we looked at the data, it was immediately clear that while both groups improved over time (a ‘main effect’ of time), there was no interaction to be found:
While it is likely that much of the increase over time can be explained by test-retest effects (i.e. simply taking the test twice), we wanted to see if any of this variance might be explained by something specific to meditation. To do this we entered stop accuracy and error-awareness into a linear model comparing the difference of slope between each group’s practice and the EAT measures. Here we saw that practice predicted stop accuracy improvement only in the meditation group, and that the this relationship was statistically greater than in the reading group:
These results lead us to conclude that while we did not observe a treatment effect of MT on the error-awareness task, the presence of strong time effects and MT-only correlation with practice suggested that the improvements within each group may relate to the “active ingredients” of MT but reflect motivation-driven artifacts in the reading group. Sadly we cannot conclude this firmly- we’d have needed to include a third passive control group for comparison. Thankfully this was pointed out to us by a kind reviewer, who noted that this argument is kind of like having one’s cake and eating it, so we’ll restrict ourselves to arguing that the EAT finding serves as a nice validation of the active control- both groups improved on something, and a potential indicator of a stop-related treatment mechanism.
While the EAT served as a behavioral measure of basic cognitive processes, we also wanted to examine the neural correlates of attention and emotion, to see how they might respond to mindfulness training in our intervention. For this we partnered with Karina Blair at the National Institute of Mental Health to bring the Affective Stroop task (shown below) to Denmark .
The Affective Stroop Task (AST) depends on a basic “number-counting Stroop” to investigate the neural correlates of attention, emotion, and their interaction. To complete the task, your instruction is simply “count the number of numbers in the first display (of numbers), count the number of numbers in the second display, and decide which display had more number of numbers”. As you can see in the trial example above, conflict in the task (trial-type “C”) is driven by incongruence between the Arabic numeral (e.g. “4”) and the numeracy of the display (a display of 5 “4”’s). Meanwhile, each trial has nasty or neutral emotional stimuli selected from the international affective picture system. Using the AST, we were able to examine the neural correlates of executive attention by contrasting task (B + C > A) and emotion (negative > neutral) trials.
Since we were especially interested in changes over time, we expanded on these contrasts to examine increased or decreased neural response between the first and last scans of the study. To do this we relied on two levels of analysis (standard in imaging), where at the “first” or “subject level” we examined differences between the two time points for each condition (task and emotion), within each subject. We then compared these time-related effects (contrast images) between each group using a two-sample t-test with total minutes of practice as a co-variate. To assess the impact of meditation on performing the AST, we examined reaction times in a model with factors group, time, task, and emotion. In this way we were able to examine the impact of MT on neural activity and behavior while controlling for the kinds of artifacts discussed in the previous section.
Our analysis revealed three primary findings. First, the reaction time analysis revealed a significant effect of MT on Stroop conflict, or the difference between reaction time to incongruent versus congruent trials. Further, we did not observe any effect on emotion-related RTs- although both groups sped up significantly to negative trials vs neutral (time effect), this increase was equivalent in both groups. Below you can see the stroop-conflict related RTs:
This became particularly interesting when we examine the neural response to these conditions, and again observed a pattern of overall [BOLD signal] increases in the dorsolateral prefrontal cortex to task performance (below):
Interestingly, we did not observe significant overall increases to emotional stimuli just being in the MT group didn’t seem to be enough to change emotional processing. However, when we examined correlations with amount practice and increased BOLD to negative emotion across the whole brain, we found a striking pattern of fronto-insular BOLD increases to negative images, similar to patterns seen in previous studies of compassion and mindfulness practice:
When we put all this together, a pattern began to emerge. Overall it seemed like MT had a relatively clear impact on attention and cognitive control. Practice-correlated increases on EAT stop accuracy, reduced Affective Stroop conflict, and increases in dorsolateral prefrontal cortex responses to task all point towards plasticity at the level of executive function. In contrast our emotion-related findings suggest that alterations in affective processing occurred only in MT participants with the most practice. Given how little we know about the training trajectories of cognitive vs affective skills, we felt that this was a very interesting result.
Conclusion: the more you do, the what you get?
For us, the first conclusion from all this was that when you control for motivation and a host of other confounds, brief MT appears to primarily train attention-related processes. Secondly, alterations in affective processing seemed to require more practice to emerge. This is interesting both for understanding the neuroscience of training and for the effective application of MT in clinical settings. While a great deal of future research is needed, it is possible that the affective system may be generally more resilient to intervention than attention. It may be the case that altering affective processes depends upon and extends increasing control over executive function. Previous research suggests that attention is largely flexible, amenable to a variety of training regimens of which MT is only one beneficial intervention. However we are also becoming increasingly aware that training attention alone does not seem to directly translate into closely related benefits.
As we begin to realize that many societal and health problems cannot be solved through medication or attention-training alone, it becomes clear that techniques to increase emotional function and well-being are crucial for future development. I am reminded of a quote overheard at the Mind & Life Summer Research Institute and attributed to the Dalai Lama. Supposedly when asked about their goal of developing meditation programs in the west, HHDL replied that, what was truly needed in the West was not “cognitive training, as (those in the west) are already too clever. What is needed rather is emotion training, to cultivate a sense of responsibility and compassion”. When we consider falling rates of empathy in medical practitioners and the link to health outcome, I think we do need to explore the role of emotional and embodied skills in supporting a wide-array of functions in cognition and well-being. While emotional development is likely to depend upon executive function, given all the recent failures to show a transfer from training these domains to even closely related ones, I suspect we need to begin including affective processes in our understanding of optimal learning. If these differences hold, then it may be important to reassess our interventions (mindful and otherwise), developing training programs that are customized in terms of the intensity, duration, and content appropriate for any given context.
Of course, rather than end on such an inspiring note, I should point out that like any study, ours is not without flaws (you’ll have to read the paper to find out how many 😉 ) and is really just an initial step. We made significant progress in replicating common neural and behavioral effects of MT while controlling for important confounds, but in retrospect the study could have been strengthened by including measures that would better distinguish the precise mechanisms, for example a measure of body awareness or empathy. Another element that struck me was how much I wish we’d had a passive control group, which could have helped flesh out how much of our time effect was instrument reliability versus motivation. As far as I am concerned, the study was a success and I am happy to have done my part to push mindfulness research towards methodological clarity and rigor. In the future I know others will continue this trend and investigate exactly what sorts of practice are needed to alter brain and behavior, and just how these benefits are accomplished.
In the near-future, I plan to give mindfulness research a rest. Not that I don’t find it fascinating or worthwhile, but rather because during the course of my PhD I’ve become a bit obsessed with interoception and meta-cognition. At present, it looks like I’ll be spending my first post-doc applying predictive coding and dynamic causal modeling to these processes. With a little luck, I might be able to build a theoretical model that could one day provide novel targets for future intervention!
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:
“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.”
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.
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:
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.
Just a quick post to give my review of the latest addition to imaging and mindfulness research. A new article by Kozasa et al, slated to appear in Neuroimage, investigates the neural correlates of attention processing in a standard color-word stroop task. A quick overview of the article reveals it is all quite standard; two groups matched for age, gender, and years of education are administered a standard RT-based (i.e. speeded) fMRI paradigm. One group has an average of 9 years “meditation experience” which is described as “a variety of OM (open monitoring) or FA (focused attention) practices such as “zazen”, mantra meditation, mindfulness of breathing, among others”. We’ll delve into why this description should give us pause for thought in a moment, for now let’s look at the results.
In a nutshell, the authors find that meditation-practitioners show faster reaction times with reduced BOLD-signal for the incongruent (compared to congruent and neutral) condition only. The regions found to be more active for non-meditators compared to meditators are the (right) “lentiform nucleus, medial frontal gyrus, and pre-central gyrus” . As this is not accompanied by any difference in accuracy, the authors interpret the finding as demonstrating that “meditators may have maintained the focus in naming the colour with less interference of reading the word and consequently have to exert less effort to monitor the conflict and less adjustment in the motor control of the impulses to choose the correct colour button.” The authors in the conclusion review related findings and mention that differences in age could have contributed to the effect.
So, what are we to make of these findings? As is my usual style, I’ll give a bulleted review of the problems that immediately stand out, and then some explanation afterwards. I’ll preface my critique by thanking the authors for their hard work; my comments are intended only for the good of our research community.
Sensible findings; increases in reaction time and decreases in bold are demonstrated in areas previously implicated in meditation research
Solid, easy to understand behavioral paradigm
Relatively strong main findings ( P< .0001)
A simple replication. We like replications!
Appears to report uncorrected p-values
Study claims to “match samples for age” yet no statistical test demonstrating no difference is shown. Qualitatively, the ages seem different enough to be cause for worry (77.8% vs 65% college graduates). Always be suspicious when a test is not given!
Extremely sparse description of style of practice, no estimate of daily practice hours given.
Reaction-time based task with no active control
I’ll preface my conclusion with something Sara Lazar, a meditation researcher and neuroimaging expert at the Harvard MGH told me last summer; we need to stop going for the “low hanging fruit of meditation research”. There are now over 20 published cross-sectional reaction-time based fMRI studies of “meditators” and “non-meditators”. Compare that to the incredibly sparse number of longitudinal, active controlled studies, and it is clear that we need to stop replicating these findings and start determining what they actually tell us. Why do we need to active control our meditation studies? For one thing, we know that reaction-time based tests are heavily based by the amount of effort one expends on the task. Effort is in turn influenced by task-demands (e.g. how you treat your participants, expectations surrounding the experiment). To give one in-press example, my colleagues Christian Gaden Jensen at the Copenhagen Neurobiology Research recently conducted a study demonstrating just how strong this confounding effect can be.
To briefly summarize, Christian recruited over 150 people for randomization to four experimental groups: mindfulness-based stress reduction (MBSR), non-mindfulness stress reduction (NMSR), wait-listed controls, and financially-motivated wait-listed controls. This last group is the truly interesting one; they were told that if they had top performance on the experimental tasks (a battery of classical reaction-time based and unspeeded perceptual threshold tasks) they’d receive a reward of approximately 100$. When Christian analyzed the data, he found that the financial incentive eliminated all reaction-time based differences between the MBSR, NMSR, and financially motivated groups! It’s important to note that this study, fully randomized and longitudinal, showed something not reflected in the bulk of published studies: that meditation may actually train more basic perceptual sensitivities rather than top-down control. This is exactly why we need to stop pursuing the low-hanging fruit of uncontrolled experimental design; it’s not telling us anything new! Meditation research is no longer exploratory.
In addition to these issues, there is another issue a bit more specific to meditation research. That is the totally sparse description of the practice- less than one sentence total, with no quantitative data! In this study we are not even told what the daily practice actually consists of, or its quality or length. These practitioners report an average of 8 years practice, yet that could be 1 hour per week of mantra meditation or 12 hours a week of non-dual zazen! These are not identical processes and our lack of knowledge for this sample severely limits our ability to assess the meaning of these findings. For the past two years (and probably longer) of the Mind & Life Summer Research Institute, Richard Davidson and others have repeatedly stated that we must move beyond studying meditation as “a loose practice of FA and OM practices including x, y, z, & and other things”. Willoughby Britton suggested at a panel discussion that all meditation papers need to have at least one contemplative scholar on them or risk rejection. It’s clear that this study was most likely not reviewed by anyone with any serious academic background in meditation research.
My supervisor Antoine Lutz and his colleague John Dunne, authors of the paper that launched the “FA/OM” distinction, have since stated emphatically that we must go beyond these general labels and start investigating effects of specific meditation practices. To quote John, we need to stop treating meditation like a “black box” if we ever want to understand the actual mechanisms behind it. While I thank the authors of this paper for their earnest contribution, we need to take this moment to be seriously skeptical. We can only start to understand processes like meditation from a scientific point of view if we are willing to hold them to the highest of scientific standards. It’s time for us to start opening the black box and looking inside.
Going through my RSS backlog today, I was excited to see Kilpatrick et al.’s “Impact of Mindfulness-Based Stress Reduction Training on Intrinsic Brain Connectivity” appear in this week’s early view Neuroimage. Although I try to keep my own work focused on primary research in cognition and connectivity, mindfulness-training (MT) is a central part of my research. Additionally, there are few published findings on intrinsic connectivity in this area. Previous research has mainly focused on between-group differences in anatomical structure (gray and white matter for example) and task-related activity. A few more recent studies have gone as far as to randomize participants into wait-listed control and MT groups.
While these studies are interesting, they are of course limited in their scope by several factors. My supervisor Antoine Lutz emphasizes that in addition to our active-controlled research here in Århus, his group at Wisconsin-Madison and others are actively preparing such datasets. Active controls are simply ‘mock’ interventions (or real ones) designed to control for every possible aspect of being involved in an intervention (placebo, community, motivation) in order to isolate the variables specific to that treatment (in this case, meditation, but not sitting, breathing, or feeling special). Active controls are important as there is a great deal of research demonstrating that cognition itself is susceptible to placebo-like motivational effects. All and all, I’ve seen several active-controlled, cognitive-behavioral studies in review that suggest we should be strongly skeptical of any non-active controlled findings. While I can’t discuss these in detail, I will mention some of these issues in my review of the neuroimage manuscript. It suffices to say however, that if you are working on a passive-controlled study in this area, you had better get it out fast as you can expect reviewers to be greatly tightening their expectations in the coming months, as more and more rigorous papers appear. As Sara Lazar put it during my visit to her lab last summer “the low-hanging fruit of MBSR brain research are rapidly vanishing”. Overall this is a good thing for the community and we’ll see why in a moment.
Now let us turn to the paper at hand. Kilpatrick et al start with a standard summary of MBSR and rsfMRI research, focusing on findings indicating MBSR trains focused attention, sensory introspection/interception and perception. They briefly review now well-established findings indicating that rsfMRI is sensitive to training related changes, including studies that demonstrate the sensitivity of the resting state to conditions such as fatigue, eyes-open vs eyes-closed, and recent sleep. This is all pretty well and good, but I think it’s a bit odd when we see just how they collect their data.
Briefly, they recruited 32 healthy adults for randomization to MBSR and waitlist controls. Controls then complete the Mindfulness Attention Awareness Scale (MAAS) and receive 8 weeks of diary-logged standard MBSR training. After training, participants are recalled for the rsfMRI scan. An important detail here is that participants are not scanned before and after training, rendering the fMRI portion of the experiment closer to a cross-section than true longitudinal design. At the time of scan, the researchers then give two ‘task-free states’, with and without auditory white noise. The authors indicate that the noise condition is included “to enable new analysis methods not conducted here”, presumably to average out scanner-noise related affects. They later indicate no differences between the two conditions, which causes me to ask how much here is meditation vs focusing-on-scanner-noise specific. Finally, they administer the ‘task free’ states with a slight twist:
“”During this baseline scan of about 5 min, we would like you to again stay as still as possible and be mindfully aware of your surroundings. Please keep your eyes closed during this procedure. Continue to be mindfully aware of whatever you notice in your surroundings and your own sensations. Mindful awareness means that you pay attention to your present moment experience, in this case the changing sounds of the scanner/changing background sounds played through the headphones, and to bring interest and curiosity to how you are responding to them.”
While the manipulation makes sense given the experimenter’s hypothesis concerning sensory processing, an ongoing controversy in resting-state research is just what it is that constitutes ‘rest’. Research here suggests that functional connectivity is sensitive to task-instructions and variations in visual stimulation, and many complain about the lack of specificity within different rest conditions. Kilpatrick et al’s manipulation makes sense given that what they really want to see is meditation-related alterations, but it’s a dangerous leap without first establishing the relationship between ‘true rest’ and their ‘auditory meditation’ condition. Research on the impact of scanner-noise indicates some degree of noise-related nuisance effects, and also some functionally significant effects. If you’ve never been in an MR experiment, the scanner is LOUD. During my first scan I actually started feeling claustrophobic due to the oppressive machine-gun like noise of the gradient coil. Anyway, it’s really troubling that Kilpatrick et al don’t include a totally task-free set for comparison, and I’m hesitant to call this a resting-state finding without further clarification.
The study is extremely interesting, but it’s important to note it’s limitations:
Lack of active control- groups are not controlled for motivation.
No pre/post scan.
Novel resting state without comparison condition.
Findings are discussed as ‘training related’ without report of correlation with reported practice hours.
Anti-correlations reported with global-signal nuisance regression. No discussion of possible regression related inducement (see edit).
Discussion of findings is unclear; reported as greater DMN x Auditory correlation, but the independent component includes large portions of the salience network.
Ultimately they identify a “auditory/salience” independent component network (ICN) (primary auditory, STG, posterior Insula, ACC, and lateral frontal cortex) and then conduct seed-regression analyses of the network with areas of the DMN and Dorsal Attention Network (DAN). I find it highly strange that they pick up a network that seems to conflate primary sensory and salience regions, as do the researchers who state “Therefore, the ICN was labeled as “auditory/salience”. It is unclear why the components split differently in our sample, perhaps the instructions that brought attention to auditory input altered the covariance structure somewhat.” Given the lack of motivational control in the study, the issues in this study begin to pile onto one another and I am not sure what we can really conclude. They further find that the MBSR group demonstrates greater “auditory/salience x DMN connectivity”, “greater visual and auditory functional connectivity” (see image below). They also report several increased anti-correlations, between the aud/sal network, dMPFC and visual regions. I find this to be an extremely tantalizing finding as it would reflect a decrease in processing automaticity amongst the SAL, CEN, and DMN networks. There are some serious problems with these kinds of analysis that the authors don’t address, and so we again must reserve any strong conclusions. Here is what Kilpatrick et al conclude:
“The current findings extend the results of prior studies that showed meditation-related changes in specific brain regions active during attention and sensory processing by providing evidence that MBSR trained compared to untrained subjects, during a focused attention instruction, have increased connectivity within sensory networks and between regions associated with attentional processes and those in the attended sensory cortex. In addition they show greater differentiation between regions associated with attentional processes and the unattended sensory cortex as well as greater differentiation between attended and unattended sensory networks”
As is typical, the list of findings is quite long and I won’t bother re-stating it all here. Given the resting instructions it seems clear that the freshly post-MBSR participants are likely to have engaged a pretty dedicated set of cognitive operations during the scan. Yet it’s totally unclear what the control group would do given these contemplative instructions. Presumably they’d just lie in the scanner and try not to tune out the noise- but you can see here how it’s not clear that these conditions are really that comparable without having some idea of what’s going on. In essence what you (might) have here is one group actually doing something (meditation) and the other group not doing much at all. Ideally you want to see how training impacts the underlying process in a comparable way. Motivation has been repeatedly linked to BOLD signal intensity and in this case, it could very well be that these findings are simple artifacts of motivation to perform. If one group is actually practicing mindfulness and the other isn’t, you have not isolated the variable of interest. The authors could have somewhat alleviated this by including data from the additional pain task (“not reported here”) and/or at least giving us a correlation of the findings with the MAAS scale. I emphasize that I do find the findings of this paper interesting- they map extremely well onto my own hypotheses about how RSNs interact with mindfulness training, but that we must interpret them with caution.
Overall I think this was a project with a strong theoretical motivation and some very interesting ideas. One problem with looking at state-mindfulness in the scanner is the cramped, noisy environment. I think Kilpatrick et al had a great idea in their attempt to use the noise itself as a manipulation. Further, the findings make a good deal of sense. Still, given the above limitation, it’s important to be really careful with our conclusions. At best, this study warrants an extremely rigorous follow-up, and I wish neuroimage had published it with a bit more information, such as the status of any rest-MAAS correlations. Anyway, this post has gotten quite long and I think I’d best get back to work- for my next post I think I’ll go into more detail about some of the issues confront resting state (what is “rest”?) and mindfulness (role of active controls for community, motivation, and placebo effects) and what they mean for resting-state research.
edit: just realized I never explained limitation #5. See my “beautiful noise” slides (previous post) regarding the controversy of global signal regression and anti-correlation. Simply put, there is somewhat convincing evidence that this procedure (designed to eliminate low-frequency nuisance co-variates) may actually mathematically induce anti-correlations where none exist, probably due to regression to the mean. While it’s not a slam-dunk (see response by Fox et al), it’s an extremely controversial area and all anti-correlative findings should be interpreted in light of this possibility.
If you like this post please let me know in the comments! If I can get away with rambling about this kind of stuff, I’ll do so more frequently.