Insula and Anterior Cingulate: the ‘everything’ network or systemic neurovascular confound?
February 18th, 2012 § 14 Comments
It’s no secret in cognitive neuroscience that some brain regions garner more attention than others. Particularly in fMRI research, we’re all too familiar with certain regions that seem to pop up in study after study, regardless of experimental paradigm. When it comes to areas like the anterior cingulate cortex (ACC) and insula (AIC), the trend is obvious. Generally when I see the same brain region involved in a wide a variety of tasks, I think there must be some very general level function which encompasses these paradigms. Off the top of my head, the ACC and AIC are major players in cognitive control, pain, emotion, consciousness, salience, working memory, decision making, and interoception to name a few. Maybe on a bad day I’ll look at a list like that and think, well localization is just all wrong, and really what we have is a big fat prefrontal cortex doing everything in conjunction. A paper published yesterday in Cerebral Cortex took my breath away and lead to a third, more sinister option: a serious methodological confound in a large majority of published fMRI papers.
Neurovascular coupling and the BOLD signal: a match not made in heaven
An important line of research in neuroimaging focuses on noise in fMRI signals. The essential problem of fMRI is that, while it provides decent spatial resolution, the data is acquired slowly and indirectly via the blood-oxygenation level dependent (BOLD) signal. The BOLD signal is messy, slow, and extremely complex in its origins. Although we typically assume increasing BOLD signal equals greater neural activity, the details of just what kind of activity (e.g. excitatory vs inhibitory, post-synaptic vs local field) are murky at best. Advancements in multi-modal and optogenetic imaging hold a great deal of promise regarding the signal’s true nature, but sadly we are currently at a “best guess” level of understanding. This weakness means that without careful experimental design, it can be difficult to rule out non-neural contributors to our fMRI signal. Setting aside the worry about what neural activity IS measured by BOLD signal, there is still the very real threat of non-neural sources like respiration and cardiovascular function confounding the final result. This is a whole field of research in itself, and is far too complex to summarize here in its entirety. The basic issue is quite simple though.
End-tidal C02, respiration, and the BOLD Signal
In a nutshell, the BOLD signal is thought to measure downstream changes in cerebral blood-flow (CBF) in response to neural activity. This relationship, between neural firing and blood flow, is called neurovascular coupling and is extremely complex, involving astrocytes and multiple chemical pathways. Additionally, it’s quite slow: typically one observes a 3-5 second delay between stimulation and BOLD response. This creates our first noise-related issue; the time between each ‘slice’ of the brain, or repetition time (TR), must be optimized to detect signals at this frequency. This means we sample from our participant’s brain slowly. Typically we sample every 3-5 seconds and construct our paradigms in ways that respect the natural time lag of the BOLD signal. Stimulate too fast, and the vasculature doesn’t have time to respond. Stimulation frequency also helps prevent our first simple confound: our pulse and respiration rates tend oscillate at slightly slower frequencies (approximately every 10-15 seconds). This is a good thing, and it means that so long as your design is well controlled (i.e. your events are properly staggered and your baseline is well defined) you shouldn’t have to worry too much about confounds. But that’s our first problematic assumption; consider for example when one’s paradigms use long blocks of obscure things like “decide how much you identify with these stimuli”. If cognitive load differs between conditions, or your groups (for example, a PTSD and a control group) react differently to the stimuli, respiration and pulse rates might easily begin to overlap your sampling frequency, confounding the BOLD signal.
But you say, my experiment is well controlled, and there’s no way my groups are breathing THAT differently! Fair enough, but this leads us to our next problem: end tidal CO2. Without getting into the complex physiology, end-tidal CO2 is a by-product of respiration. When you hold your breath, CO2 blood levels rise dramatically. CO2 is a potent vasodilator, meaning it opens blood vessels and increases local blood flow. You’ve probably guessed where I’m going with this: hold your breath in the fMRI and you get massive alterations in the BOLD signal. Your participants don’t even need to match the sampling frequency of the paradigm to confound the BOLD; they simply need to breath at slightly different rates in each group or condition and suddenly your results are full of CO2 driven false positives! This is a serious problem for any kind of unconstrained experimental design, especially those involving poorly conceptualized social tasks or long periods of free activity. Imagine now that certain regions of the brain might respond differently to levels of CO2.
This image is from Change & Glover’s paper, “Relationship between respiration, end-tidal CO2, and BOLD signals in resting-state fMRI”. Here they measure both CO2 and respiration frequency during a standard resting-state scan. The image displays the results of group-level regression of these signals with BOLD. I’ve added circles in blue around the areas that respond the strongest. Without consulting an atlas, we can clearly see that bilateral anterior insula extending upwards into parietal cortex, anterior cingulate, and medial-prefrontal regions are hugely susceptible to respiration and CO2. This is pretty damning for resting-state fMRI, and makes sense given that resting state fluctuations occur at roughly the same rate as respiration. But what about well-controlled event related designs? Might variability in neurovascular coupling cause a similar pattern of response? Here is where Di et al’s paper lends a somewhat terrifying result:
Di et al recently investigated the role of vascular confounds in fMRI by administrating a common digit-symbol substitution task (DSST), a resting state, and a breath-holding paradigm. Signals related to resting-state and breath-holding were then extracted and entered into multiple regression with the DSST-related activations. This allowed Di et al to estimate what brain regions were most influenced by low-frequency fluctuation (ALFF, a common resting state measure) and purely vascular sources (breath-holding). From the figure above, you can see that regions marked with the blue arrow were the most suppressed, meaning the signal explained by the event-related model was significantly correlated with the covariates, and in red where the signal was significantly improved by removal of the covariates. The authors conclude that “(results) indicated that the adjustment tended to suppress activation in regions that were near vessels such as midline cingulate gyrus, bilateral anterior insula, and posterior cerebellum.” It seems that indeed, our old friends the anterior insula and cingulate cortex are extremely susceptible to neurovascular confound.
What does this mean for cognitive neuroscience? For one, it should be clear that even well-controlled fMRI designs can exhibit such confounds. This doesn’t mean we should throw the baby out with the bathwater though; some designs are better than others. Thankfully it’s pretty easy to measure respiration with most scanners, and so it is probably a good idea at minimum to check if one’s experimental conditions do indeed create differential respiration patterns. Further, we need to be especially cautious in cases like meditation or clinical fMRI, where special participant groups may have different baseline respiration rates or stronger parasympathetic responses to stimuli. Sadly, I’m afraid that looking back, these findings greatly limit our conclusions in any design that did not control for these issues. Remember that the insula and ACC are currently cognitive neuroscience’s hottest regions. I’m not even going to get into resting state, where these problems are all magnified 10 fold. I’ll leave you with this image from neuroskeptic, estimating the year’s most popular brain regions:
Are those spikes publication fads, every-task regions, or neurovascular artifacts? You be the judge.
edit:As many of you had questions or comments regarding the best way to deal with respiratory related issues, I spoke briefly with resident noise expert Torben Lund at yesterday’s lab meeting. Removal of respiratory noise is fairly simple, but the real problem is with end-tidal C02. According to Torben, most noise experts agree that regression techniques only partially remove the artifact, and that an unknown amount is left behind even following signal regression. This may be due to slow vascular saturation effects that build up and remain irrespective of shear breath frequency. A very tricky problem indeed, and certainly worth researching. Note: credit goes to my methods teacher and fMRI noise expert Torben Lund, and CFIN neurobiologist Rasmus Aamand, for introducing and explaining the basis of the C02/respiration issue to me. Rasmus particularly, whose sharp comments lead to my including respiration and pulse measures in my last meditation project.Neuroscientists: What’s the most interesting question right now?
February 14th, 2012 § 10 Comments
After 20 years of cognitive neuroscience, I sometimes feel frustrated by how little progress we’ve made. We still struggle with basic issues, like how to ask a subject if he’s in pain, or what exactly our multi-million dollar scanners measure. We lack a unifying theory linking information, psychological function, and neuroscientific measurement. We still publish all kinds of voodoo correlations, uncorrected p-values, and poorly operationalized blobfests. Yet, we’ve also laid some of the most important foundational research of our time. In twenty years we’ve mapped a mind boggling array of cognitive function. Some of these attempts at localization may not hold; others may be built on shaky functional definitions or downright poor methods. Even in the face of this uncertainty, the shear number and variety of functions that have been mapped is inspiring. Further, we’ve developed analytic tools to pave the way for an exciting new decade of multi-modal and connectomic research. Developments like resting-state fMRI, optogenetics, real time fMRI, and multi-modal imaging, make for a very exciting time to be a Cognitive Neuroscientist!
Online, things can seem a bit more pessimistic. Snarky methods blogs dedicated to revealing the worst in field tend to do well, and nearly any social-media savy neurogeek will lament the depressing state of science journalism and the brain. While I am also tired of incessantly phrenological, blob-obsessed reports (“research finds god spot in the brain, are your children safe??”) I think we share some of the blame for not communicating properly about what interests and challenges us. For me, some of the most exciting areas of research are those concerning getting straight about what our measurements mean- see the debates over noise in resting state or the neural underpinnings of the BOLD signal for example. Yet these issues are often reported as dry methodological reports, the writers themselves seemingly bored with the topic.
We need to do a better job illustrating to people just how complex and infantile our field is. The big, sexy issues are methodological in nature. They’re also phenomenological in nature. Right now neuroscience is struggling to define itself, unsure if we should be asking our subjects how they feel or anesthetizing them. I believe that if we can illustrate just how tenuous much of our research is, including the really nagging problems, the public will better appreciate seemingly nuanced issues like rest-stimulus interaction and noise-regression.
With that in mind- what are your most exciting questions, right now? What nagging thorn ails you at all steps in your research?
For me, the most interesting and nagging question is, what do people do when we ask them to do nothing? I’m talking about rest-stimulus interaction and mind wandering. There seem to be two prevailing (pro-resting state) views: that default mode network-related activity is related to subjective mind-wandering, and/or that it’s a form of global, integrative, stimulus independent neural variability. On the first view, variability in participants ability to remain on-task drive slow alterations in behavior and stimulus-evoked brain activity. On the other, innate and spontaneous rhythms synchronize large brain networks in ways that alter stimulus processing and enable memory formation. Either way, we’re left with the idea that a large portion of our supposedly well-controlled, stimulus-related brain activity is in fact predicted by uncontrolled intrinsic brain activity. Perhaps even defined by it! When you consider that all this is contingent on the intrinsic activity being real brain activity and not some kind of vascular or astrocyte-driven artifact, every research paradigm becomes a question of rest-stimulus interaction!
So neuroscientists, what keeps you up at night?
A brave new default mode in meditation practitioners- or just confused controls? Review of Brewer (2011)
February 8th, 2012 § 5 Comments
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:
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:
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.
