Make sure you are one of the pilot subjects. It’s amazing what kind of things you notice when you’re actually in the scanner that you never otherwise would – anything from the fact that the stimuli aren’t very visible, to the fact that the sequence you’re using makes the bed shake, to the fact that the task is just so long & boring that you fall asleep by the end (which is so much easier in the scanner than when you’re sitting up at a computer, which is when you probably piloted the task!)

If you’re not MRI safe, get a trusted fellow researcher to do it. But never assume that non-scientist volunteers will tell you these things because they don’t (I think because they don’t want to look stupid by questioning your authority.)

Thanks for your comment. After further discussion with Torben, I should probably remove my comment that noise filtration is simple, as it’s anything but. While the common methods for dealing with it are fairly straight forward- for example adding a column to the design matrix to model respiration-related effects- such approaches cannot account for residual artifacts relating to spin-history effects and end-tidal C02. While regression of respiration-related movement is fairly simple, it appears to often underperform and can often strip important signal from your data. Band-pass filtering is one common standby which removes high and low frequency noise. However it’s not clear that saturation effects from end-tidal C02 are covered by this method; Torben says that even when attempting to remove the noise via the GLM, a good deal of noise signal is left behind. The truth is, our best methods seem to make little difference at best, and at worst will totally strip all interesting signal from your data. So the problem is far from solved and various techniques all come with harsh trade-offs.

Best,
Micah

What do you mean when you state that “removal of respiratory noise is fairly simple”? Do you mean that the mathematical operation is simple or well understood? Do you mean that it is effective? Although it is nice when a mathematical operation is simple and/or well understood it doesn’t amount to a hill of beans if it isn’t effective. So where is the evidence that the filtering of respiratory noise by present means is effective?

And by the way, what is the accepted means of removing the respiratory noise? Is it through band-pass filtering of Fourier frequency components? Is it through wavelet filtering of scale and temporal focality? Is it through statistical methods which attempt to account for modeled confounds and associated measurements?

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

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

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

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

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

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

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

Best,
Micah

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

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

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

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

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

Sincerely, Judson Brewer