Tag: methods

bio-, chemo-, neuro-, eco-informatics… why no psycho-?

The latest issue of the APS Observer features a special section on methods. I contributed a piece discussing the need for a full-fledged discipline of psychoinformatics:

Scientific progress depends on our ability to harness and apply modern information technology. Many advances in the biological and social sciences now emerge directly from advances in the large-scale acquisition, management, and synthesis of scientific data. The application of information technology to science isn’t just a happy accident; it’s also a field in its own right — one commonly referred to as informatics. Prefix that term with a Greek root or two and you get other terms like bioinformatics, neuroinformatics, and ecoinformatics — all well-established fields responsible for many of the most exciting recent discoveries in their parent disciplines.

Curiously, following the same convention also gives us a field called psychoinformatics — which, if you believe Google, doesn’t exist at all (a search for the term returns only 500 hits as of this writing; Figure 1). The discrepancy is surprising, because labels aside, it’s clear that psychological scientists are already harnessing information technology in powerful and creative ways — often reshaping the very way we collect, organize, and synthesize our data.

Here’s the picture that’s worth, oh, at least ten or fifteen words:

Figure 1. Number of Google search hits for informatics-related terms, by prefix.

You can read the rest of the piece here if you’re so inclined. Check out some of the other articles too; I particularly like Denny Borsboom’s piece on network analysis. EDIT: and Anna Mikulak’s piece on optogenetics! I forgot the piece on optogenetics! How can you not love optogenetics!

a human and a monkey walk into an fMRI scanner…

Tor Wager and I have a “news and views” piece in Nature Methods this week; we discuss a paper by Mantini and colleagues (in the same issue) introducing a new method for identifying functional brain homologies across different species–essentially, identifying brain regions in humans and monkeys that seem to do roughly the same thing even if they’re not located in the same place anatomically. Mantini et al make some fairly strong claims about what their approach tells us about the evolution of the human brain (namely, that some cortical regions have undergone expansion relative to monkeys, while others have adapted substantively new functions). For reasons we articulate in our commentary, I’m personally not so convinced by the substantive conclusions, but I do think the core idea underlying the method is a very clever and potentially useful one:

Their technique, interspecies activity correlation (ISAC), uses functional magnetic resonance imaging (fMRI) to identify brain regions in which humans and monkeys exposed to the same dynamic stimulus—a 30-minute clip from the movie The Good, the Bad and the Ugly—show correlated patterns of activity (Fig. 1). The premise is that homologous regions should have similar patterns of activity across species. For example, a brain region sensitive to a particular configuration of features, including visual motion, hands, faces, object and others, should show a similar time course of activity in both species—even if its anatomical location differs across species and even if the precise features that drive the area’s neurons have not yet been specified.

Mo Costandi has more on the paper in an excellent Guardian piece (and I’m not just saying that because he quoted me a few times). All in all, I think it’s a very exciting method, and it’ll be interesting to see how it’s applied in future studies. I think there’s a fairly broad class of potential applications based loosely around the same idea of searching for correlated patterns. It’s an idea that’s already been used by Uri Hasson (an author on the Mantini et al paper) and others fairly widely in the fMRI literature to identify functional correspondences across different subjects; but you can easily imagine conceptually similar applications in other fields too–e.g., correlating gene expression profiles across species in order to identify structural homologies (actually, one could probably try this out pretty easily using the mouse and human data available in the Allen Brain Atlas).

ResearchBlogging.orgMantini D, Hasson U, Betti V, Perrucci MG, Romani GL, Corbetta M, Orban GA, & Vanduffel W (2012). Interspecies activity correlations reveal functional correspondence between monkey and human brain areas. Nature methods PMID: 22306809

Wager, T., & Yarkoni, T. (2012). Establishing homology between monkey and human brains Nature Methods DOI: 10.1038/nmeth.1869

does functional specialization exist in the language system?

One of the central questions in cognitive neuroscience–according to some people, at least–is how selective different chunks of cortex are for specific cognitive functions. The paradigmatic examples of functional selectivity are pretty much all located in sensory cortical regions or adjacent association cortices. For instance, the fusiform face area (FFA), is so named because it (allegedly) responds selectively to faces but not to other stimuli. Other regions with varying selectivity profiles are similarly named: the visual word form area (VWFA), parahippocampal place area (PPA), extrastriate body area (EBA), and so on.

In a recent review paper, Fedorenko and Kanwisher (2009) sought to apply insights from the study of functionally selective visual regions to the study of language. They posed the following question with respect to the neuroimaging of language in the title of their paper: Why hasn’t a clearer picture emerged? And they gave the following answer: it’s because brains differ from one another, stupid.

Admittedly, I’m paraphrasing; they don’t use exactly those words. But the basic point they make is that it’s difficult to identify functionally selective regions when you’re averaging over a bunch of very different brains. And the solution they propose–again, imported from the study of visual areas–is to identify potentially selective language regions-of-interest (ROIs) on a subject-specific basis rather than relying on group-level analyses.

The Fedorenko and Kanwisher paper apparently didn’t please Greg Hickok of Talking Brains, who’s done a lot of very elegant work on the neurobiology of language.  A summary of Hickok’s take:

What I found a bit on the irritating side though was the extremely dim and distressingly myopic view of progress in the field of the neural basis of language.

He objects to Fedorenko and Kanwisher on several grounds, and the post is well worth reading. But since I’m very lazy tired, I’ll just summarize his points as follows:

  • There’s more functional specialization in the language system than F&K give the field credit for
  • The use of subject-specific analyses in the domain of language isn’t new, and many researchers (including Hickok) have used procedures similar to those F&K recommend in the past
  • Functional selectivity is not necessarily a criterion we should care about all that much anyway

As you might expect, F&K disagree with Hickok on these points, and Hickok was kind enough to post their response. He then responded to their response in the comments (which are also worth reading), which in turn spawned a back-and-forth with F&K, a cameo by Brad Buchsbaum (who posted his own excellent thoughts on the matter here), and eventually, an intervention by a team of professional arbitrators. Okay, I made that last bit up; it was a very civil disagreement, and is exactly what scientific debates on the internet should look like, in my opinion.

Anyway, rather than revisit the entire thread, which you can read for yourself, I’ll just summarize my thoughts:

  • On the whole, I think my view lines up pretty closely with Hickok’s and Buchsbaum’s. Although I’m very far from an expert on the neurobiology of language (is there a word in English for someone’s who’s the diametric opposite of an expert–i.e., someone who consistently and confidently asserts exactly the wrong thing? Cause that’s what I am), I agree with Hickok’s argument that the temporal poles show a response profile that looks suspiciously like sentence- or narrative-specific processing (I have a paper on the neural mechanisms of narrative comprehension that supports that claim to some extent), and think F&K’s review of the literature is probably not as balanced as it could have been.
  • More generally, I agree with Hickok that demonstrating functional specialization isn’t necessarily that important to the study of language (or most other domains). This seems to be a major point of contention for F&K, but I don’t think they make a very strong case for their view. They suggest that they “are not sure what other goals (besides understanding a region’s computations) could drive studies aimed at understanding how functionally specialized a region is,” which I think is reasonable, but affirms the consequent. Hickok isn’t saying there’s no reason to search for functional specialization in the F&K sense; as I read him, he’s simply saying that you can study the nature of neural computation in lots of interesting ways that don’t require you to demonstrate functional specialization to the degree F&K seem to require. Seems hard to disagree with that.
  • Buchsbaum points out that it’s questionable whether there are any brain regions that meet the criteria F&K set out for functional specialization–namely that “A brain region R is specialized for cognitive function x if this region (i) is engaged in tasks that rely on cognitive function x, and (ii) is not engaged in tasks that do not rely on cognitive function x.Buchsbaum and Hickok both point out that the two examples F&K give of putatively specialized regions (the FFA and the temporo-parietal junction, which some people believe is selectively involved in theory of mind) are hardly uncontroversial. Plenty of people have argued that the FFA isn’t really selective to faces, and even more people have argued that the TPJ isn’t selective to theory of mind. As far as I can tell, F&K don’t really address this issue in the comments. They do refer to a recent paper of Kanwisher’s that discusses the evidence for functional specificity in the FFA, but I’m not sure the argument made in that paper is itself uncontroversial, and in any case, Kanwisher does concede that there’s good evidence for at least some representation of non-preferred stimuli (i.e., non-faces in the FFA). In any case, the central question here is whether or not F&K really unequivocally believe that FFA and TPJ aren’t engaged by any tasks that don’t involve face or theory of mind processing. If not, then it’s unfair to demand or expect the same of regions implicated in language.
  • Although I think there’s a good deal to be said for subject-specific analyses, I’m not as sanguine as F&K that a subject-specific approach offers a remedy to the problems that they perceive afflict the study of the neural mechanisms of language. While there’s no denying that group analyses suffer from a number of limitations, subject-specific analyses have their own weaknesses, which F&K don’t really mention in their paper. One is that such analyses typically require the assumption that two clusters located in slightly different places for different subjects must be carrying out the same cognitive operations if they respond similarly to a localizer task. That’s a very strong assumption for which there’s very little evidence (at least in the language domain)–especially because the localizer task F&K promote in this paper involves a rather strong manipulation that may confound several different aspects of language processing.
    Another problem is that it’s not at all obvious how you determine which regions are the “same” (in their 2010 paper, F&K argue for an algorithmic parcellation approach, but the fact that you get sensible-looking results is no guarantee that your parcellation actually reflects meaningful functional divisions in individual subjects). And yet another is that serious statistical problems can arise in cases where one or more subjects fail to show activation in a putative region (which is generally the norm rather than the exception). Say you have 25 subjects in your sample, and 7 don’t show activation anywhere in a region that can broadly be called Broca’s area. What do you do? You can’t just throw those subjects out of the analysis, because that would grossly and misleadingly inflate your effect sizes. Conversely, you can’t just identify any old region that does activate and lump it in with the regions identified in all the other subjects. This is a very serious problem, but it’s one that group analyses, for all their weaknesses, don’t have to contend with.

Disagreements aside, I think it’s really great to see serious scientific discussion taking place in this type of forum. In principle, this is the kind of debate that should be resolved (or not) in the peer-reviewed literature; in practice, peer review is slow, writing full-blown articles takes time, and journal space is limited. So I think blogs have a really important role to play in scientific communication, and frankly, I envy Hickok and Poeppel for the excellent discussion they consistently manage to stimulate over at Talking Brains!

time-on-task effects in fMRI research: why you should care

There’s a ubiquitous problem in experimental psychology studies that use behavioral measures that require participants to make speeded responses. The problem is that, in general, the longer people take to do something, the more likely they are to do it correctly. If I have you do a visual search task and ask you to tell me whether or not a display full of letters contains a red ‘X’, I’m not going to be very impressed that you can give me the right answer if I let you stare at the screen for five minutes before responding. In most experimental situations, the only way we can learn something meaningful about people’s capacity to perform a task is by imposing some restriction on how long people can take to respond. And the problem that then presents is that any changes we observe in the resulting variable we care about (say, the proportion of times you successfully detect the red ‘X’) are going to be confounded with the time people took to respond. Raise the response deadline and performance goes up; shorten it and performance goes down.

This fundamental fact about human performance is commonly referred to as the speed-accuracy tradeoff. The speed-accuracy tradeoff isn’t a law in any sense; it allows for violations, and there certainly are situations in which responding quickly can actually promote accuracy. But as a general rule, when researchers run psychology experiments involving response deaadlines, they usually work hard to rule out the speed-accuracy tradeoff as an explanation for any observed results. For instance, if I have a group of adolescents with ADHD do a task requiring inhibitory control, and compare their performance to a group of adolescents without ADHD, I may very well find that the ADHD group performs more poorly, as reflected by lower accuracy rates. But the interpretation of that result depends heavily on whether or not there are also any differences in reaction times (RT). If the ADHD group took about as long on average to respond as the non-ADHD group, it might be reasonable to conclude that the ADHD group suffers a deficit in inhibitory control: they take as long as the control group to do the task, but they still do worse. On the other hand, if the ADHD group responded much faster than the control group on average, the interpretation would become more complicated. For instance, one possibility would be that the accuracy difference reflects differences in motivation rather than capacity per se. That is, maybe the ADHD group just doesn’t care as much about being accurate as about responding quickly. Maybe if you motivated the ADHD group appropriately (e.g., by giving them a task that was intrinsically interesting), you’d find that performance was actually equivalent across groups. Without explicitly considering the role of reaction time–and ideally, controlling for it statistically–the types of inferences you can draw about underlying cognitive processes are somewhat limited.

An important point to note about the speed-accuracy tradeoff is that it isn’t just a tradeoff between speed and accuracy; in principle, any variable that bears some systematic relation to how long people take to respond is going to be confounded with reaction time. In the world of behavioral studies, there aren’t that many other variables we need to worry about. But when we move to the realm of brain imaging, the game changes considerably. Nearly all fMRI studies measure something known as the blood-oxygen-level-dependent (BOLD) signal. I’m not going to bother explaining exactly what the BOLD signal is (there are plenty of other excellent explanations at varying levels of technical detail, e.g., here, here, or here); for present purposes, we can just pretend that the BOLD signal is basically a proxy for the amount of neural activity going on in different parts of the brain (that’s actually a pretty reasonable assumption, as emerging studies continue to demonstrate). In other words, a simplistic but not terribly inaccurate model is that when neurons in region X increase their firing rate, blood flow in region X also increases, and so in turn does the BOLD signal that fMRI scanners detect.

A critical question that naturally arises is just how strong the temporal relation is between the BOLD signal and underlying neuronal processes. From a modeling perspective, what we’d really like is a system that’s completely linear and time-invariant–meaning that if you double the duration of a stimulus presented to the brain, the BOLD response elicited by that stimulus also doubles, and it doesn’t matter when the stimulus is presented (i.e., there aren’t any funny interactions between different phases of the response, or with the responses to other stimuli). As it turns out, the BOLD response isn’t perfectly linear, but it’s pretty close. In a seminal series of studies in the mid-90s, Randy Buckner, Anders Dale and others showed that, at least for stimuli that aren’t presented extremely rapidly (i.e., a minimum of 1 – 2 seconds apart), we can reasonably pretend that the BOLD response sums linearly over time without suffering any serious ill effects. And that’s extremely fortunate, because it makes modeling brain activation with fMRI much easier to do. In fact, the vast majority of fMRI studies, which employ what are known as rapid event-related designs, implicitly assume linearity. If the hemodynamic response wasn’t approximately linear, we would have to throw out a very large chunk of the existing literature–or at least seriously question its conclusions.

Aside from the fact that it lets us model things nicely, the assumption of linearity has another critical, but underappreciated, ramification for the way we do fMRI research. Which is this: if the BOLD response sums approximately linearly over time, it follows that two neural responses that have the same amplitude but differ in duration will produce BOLD responses with different amplitudes. To characterize that visually, here’s a figure from a paper I published with Deanna Barch, Jeremy Gray, Tom Conturo, and Todd Braver last year:

plos_one_figure1

Each of these panels shows you the firing rates and durations of two hypothetical populations of neurons (on the left), along with the (observable) BOLD response that would result (on the right). Focus your attention on panel C first. What this panel shows you is what, I would argue, most people intuitively think of when they come across a difference in activation between two conditions. When you see time courses that clearly differ in their amplitude, it’s very natural to attribute a similar difference to the underlying neuronal mechanisms, and suppose that there must just be more firing going on in one condition than the other–where ‘more’ is taken to mean something like “firing at a higher rate”.

The problem, though, is that this inference isn’t justified. If you look at panel B, you can see that you get exactly the same pattern of observed differences in the BOLD response even when the amplitude of neuronal activation is identical, simply because there’s a difference in duration. In other words, if someone shows you a plot of two BOLD time courses for different experimental conditions, and one has a higher amplitude than the other, you don’t know whether that’s because there’s more neuronal activation in one condition than the other, or if processing is identical in both conditions but simply lasts longer in one than in the other. (As a technical aside, this equivalence only holds for short trials, when the BOLD response doesn’t have time to saturate. If you’re using longer trials–say 4 seconds more more–then it becomes fairly easy to tell apart changes in duration from changes in amplitude. But the vast majority of fMRI studies use much shorter trials, in which case the problem I describe holds.)

Now, functionally, this has some potentially very serious implications for the inferences we can draw about psychological processes based on observed differences in the BOLD response. What we would usually like to conclude when we report “more” activation for condition X than condition Y is that there’s some fundamental difference in the nature of the processes involved in the two conditions that’s reflected at the neuronal level. If it turns out that the reason we see more activation in one condition than the other is simply that people took longer to respond in one condition than in the other, and so were sustaining attention for longer, that can potentially undermine that conclusion.

For instance, if you’re contrasting a feature search condition with a conjunction search condition, you’re quite likely to observe greater activation in regions known to support visual attention. But since a central feature of conjunction search is that it takes longer than a feature search, it could theoretically be that the same general regions support both types of search, and what we’re seeing is purely a time-on-task effect: visual attention regions are activated for longer because it takes longer to complete the conjunction search, but these regions aren’t doing anything fundamentally different in the two conditions (at least at the level we can see with fMRI). So this raises an issue similar to the speed-accuracy tradeoff we started with. Other things being equal, the longer it takes you to respond, the more activation you’ll tend to see in a given region. Unless you explicitly control for differences in reaction time, your ability to draw conclusions about underlying neuronal processes on the basis of observed BOLD differences may be severely hampered.

It turns out that very few fMRI studies actually control for differences in RT. In an elegant 2008 study discussing different ways of modeling time-varying signals, Jack Grinband and colleagues reviewed a random sample of 170 studies and found that, “Although response times were recorded in 82% of event-related studies with a decision component, only 9% actually used this information to construct a regression model for detecting brain activity”. Here’s what that looks like (Panel C), along with some other interesting information about the procedures used in fMRI studies:

grinband_figure
So only one in ten studies made any effort to control for RT differences; and Grinband et al argue in their paper that most of those papers didn’t model RT the right way anyway (personally I’m not sure I agree; I think there are tradeoffs associated with every approach to modeling RT–but that’s a topic for another post).

The relative lack of attention to RT differences is particularly striking when you consider what cognitive neuroscientists do care a lot about: differences in response accuracy. The majority of researchers nowadays make a habit of discarding all trials on which participants made errors. The justification we give for this approach–which is an entirely reasonable one–is that if we analyzed correct and incorrect trials together, we’d be confounding the processes we care about (e.g., differences between conditions) with activation that simply reflects error-related processes. So we drop trials with errors, and that gives us cleaner results.

I suspect that the reasons for our concern with accuracy effects but not RT effects in fMRI research are largely historical. In the mid-90s, when a lot of formative cognitive neuroscience was being done, people (most of them then located in Pittsburgh, working in Jonathan Cohen‘s group) discovered that the brain doesn’t like to make errors. When people make mistakes during task performance, they tend to recognize that fact; on a neural level, frontoparietal regions implicated in goal-directed processing–and particularly the anterior cingulate cortex–ramp up activation substantially. The interpretation of this basic finding has been a source of much contention among cognitive neuroscientists for the past 15 years, and remains a hot area of investigation. For present purposes though, we don’t really care why error-related activation arises; the point is simply that it does arise, and so we do the obvious thing and try to eliminate it as a source of error from our analyses. I suspect we don’t do the same for RT not because we lack principled reasons to, but because there haven’t historically been clear-cut demonstrations of the effects of RT differences on brain activation.

The goal of the 2009 study I mentioned earlier was precisely to try to quantify those effects. The hypothesis my co-authors and I tested was straightforward: if brain activity scales approximately linearly with RT (as standard assumptions would seem to entail), we should see a strong “time-on-task” effect in brain areas that are associated with the general capacity to engage in goal-directed processing. In other words, on trials when people take longer to respond, activation in frontal and parietal regions implicated in goal-directed processing and cognitive control should increase. These regions are often collectively referred to as the “task-positive” network (Fox et al., 2005), in reference to the fact that they tend to show activation increases any time people are engaging in goal-directed processing, irrespective of the precise demands of the task. We figured that identifying a time-on-task effect in the task-positive network would provide a nice demonstration of the relation between RT differences and the BOLD response, since it would underscore the generality of the problem.

Concretely, what we did was take five datasets that were lying around from previous studies, and do a multi-study analysis focusing specifically on RT-related activation. We deliberately selected studies that employed very different tasks, designs, and even scanners, with the aim of ensuring the generalizability of the results. Then, we identified regions in each study in which activation covaried with RT on a trial-by-trial basis. When we put all of the resulting maps together and picked out only those regions that showed an association with RT in all five studies, here’s the map we got:

plos_one_figure2

There’s a lot of stuff going on here, but in the interest of keeping this post short slightly less excruciatingly long, I’ll stick to the frontal areas. What we found, when we looked at the timecourse of activation in those regions, was the predicted time-on-task effect. Here’s a plot of the timecourses from all five studies for selected regions:

plos_one_figure4

If you focus on the left time course plot for the medial frontal cortex (labeled R1, in row B), you can see that increases in RT are associated with increased activation in medial frontal cortex in all five studies (the way RT effects are plotted here is not completely intuitive, so you may want to read the paper for a clearer explanation). It’s worth pointing out that while these regions were all defined based on the presence of an RT effect in all five studies, the precise shape of that RT effect wasn’t constrained; in principle, RT could have exerted very different effects across the five studies (e.g., positive in some, negative in others; early in some, later in others; etc.). So the fact that the timecourses look very similar in all five studies isn’t entailed by the analysis, and it’s an independent indicator that there’s something important going on here.

The clear-cut implication of these findings is that a good deal of BOLD activation in most studies can be explained simply as a time-on-task effect. The longer you spend sustaining goal-directed attention to an on-screen stimulus, the more activation you’ll show in frontal regions. It doesn’t much matter what it is that you’re doing; these are ubiquitous effects (since this study, I’ve analyzed many other datasets in the same way, and never fail to find the same basic relationship). And it’s worth keeping in mind that these are just the regions that show common RT-related activation across multiple studies; what you’re not seeing are regions that covary with RT only within one (or for that matter, four) studies. I’d argue that most regions that show involvement in a task are probably going to show variations with RT. After all, that’s just what falls out of the assumption of linearity–an assumption we all depend on in order to do our analyses in the first place.

Exactly what proportion of results can be explained away as time-on-task effects? That’s impossible to determine, unfortunately. I suspect that if you could go back through the entire fMRI literature and magically control for trial-by-trial RT differences in every study, a very large number of published differences between experimental conditions would disappear. That doesn’t mean those findings were wrong or unimportant, I hasten to note; there are many cases in which it’s perfectly appropriate to argue that differences between conditions should reflect a difference in quantity rather than quality. Still, it’s clear that in many cases that isn’t the preferred interpretation, and controlling for RT differences probably would have changed the conclusions. As just one example, much of what we think of as a “conflict” effect in the medial frontal cortex/anterior cingulate could simply reflect prolonged attention on high-conflict trials. When you’re experiencing cognitive difficulty or conflict, you tend to slow down and take longer to respond, which is naturally going to produce BOLD increases that scale with reaction time. The question as to what remains of the putative conflict signal after you control for RT differences is one that hasn’t really been adequately addressed yet.

The practical question, of course, is what we should do about this. How can we minimize the impact of the time-on-task effect on our results, and, in turn, on the conclusions we draw? I think the most general suggestion is to always control for reaction time differences. That’s really the only way to rule out the possibility that any observed differences between conditions simply reflect differences in how long it took people to respond. This leaves aside the question of exactly how one should model out the effect of RT, which is a topic for another time (though I discuss it at length in the paper, and the Grinband paper goes into even more detail). Unfortunately, there isn’t any perfect solution; as with most things, there are tradeoffs inherent in pretty much any choice you make. But my personal feeling is that almost any approach one could take to modeling RT explicitly is a big step in the right direction.

A second, and nearly as important, suggestion is to not only control for RT differences, but to do it both ways. Meaning, you should run your model both with and without an RT covariate, and carefully inspect both sets of results. Comparing the results across the two models is what really lets you draw the strongest conclusions about whether activation differences between two conditions reflect a difference of quality or quantity. This point applies regardless of which hypothesis you favor: if you think two conditions draw on very similar neural processes that differ only in degree, your prediction is that controlling for RT should make effects disappear. Conversely, if you think that a difference in activation reflects the recruitment of qualitatively different processes, you’re making the prediction that the difference will remain largely unchanged after controlling for RT. Either way, you gain important information by comparing the two models.

The last suggestion I have to offer is probably obvious, and not very helpful, but for what it’s worth: be cautious about how you interpret differences in activation any time there are sizable differences in task difficulty and/or mean response time. It’s tempting to think that if you always analyze only trials with correct responses and follow the suggestions above to explicitly model RT, you’ve done all you need in order to perfectly control for the various tradeoffs and relationships between speed, accuracy, and cognitive effort. It really would be nice if we could all sleep well knowing that our data have unambiguous interpretations. But the truth is that all of these techniques for “controlling” for confounds like difficulty and reaction time are imperfect, and in some cases have known deficiencies (for instance, it’s not really true that throwing out error trials eliminates all error-related activation from analysis–sometimes when people don’t know the answer, they guess right!). That’s not to say we should stop using the tools we have–which offer an incredibly powerful way to peer inside our gourds–just that we should use them carefully.

ResearchBlogging.org

Yarkoni T, Barch DM, Gray JR, Conturo TE, & Braver TS (2009). BOLD correlates of trial-by-trial reaction time variability in gray and white matter: a multi-study fMRI analysis. PloS one, 4 (1) PMID: 19165335

Grinband J, Wager TD, Lindquist M, Ferrera VP, & Hirsch J (2008). Detection of time-varying signals in event-related fMRI designs. NeuroImage, 43 (3), 509-20 PMID: 18775784

the perils of digging too deep

Another in a series of posts supposedly at the intersection of fiction and research methods, but mostly just an excuse to write ridiculous stories and pretend they have some sort of moral.


Dr. Rickles the postdoc looked a bit startled when I walked into his office. He was eating a cheese sandwich and watching a chimp on a motorbike on his laptop screen.

“YouTube again?” I asked.

“Yes,” he said. “It’s lunch.”

“It’s 2:30 pm,” I said, pointing to my watch.

“Still my lunch hours.”

Lunch hours for Rickles were anywhere from 11 am to 4 pm. It depended on exactly when you walked in on him doing something he wasn’t supposed to; that was the event that marked the onset of Lunch.

“Fair enough,” I said. “I just stopped by to see how things were going.”

“Oh, quite well.” said Rickles. “Things are going well. I just found a video of a chimp and a squirrel riding a motorbike together. They aren’t even wearing helmets! I’ll send you the link.”

“Please don’t. I don’t like squirrels. But I meant with work. How’s the data looking.”

He shot me a pained look, like I’d just caught him stealing video game money from his grandmother.

“The data are TERRIBLE,” he said in all capital letters.

I wasn’t terribly surprised at the revelation; I’d handed Rickles the dataset only three days prior, taking care not to  tell him it was the dataset from hell. Rickles was the fourth or fifth person in the line of succession; the data had been handed down from postdoc to graduate student to postdoc for several years now. Everyone in the lab wanted to take a crack at it when they first heard about it, and no one in the lab wanted anything to do with it once they’d taken a peek. I’d given it to Rickles in part to teach him a lesson; he’d been in the lab for several weeks now and somehow still seemed happy and self-assured.

“Haven’t found anything interesting yet?” I asked. “I thought maybe if you ran the Flimflan test on the A-trax, you might get an effect. Or maybe if you jimmied the cryptos on the Borgatron…”

“No, no,” Rickles interrupted, waved me off. “The problem isn’t that there’s nothing interesting in the data; it’s that there’s too MUCH stuff. There are too MANY results. The story is too COMPLEX.”

That didn’t compute for me, so I just stared at him blankly. No one ever found COMPLEX effects in my lab. We usually stopped once we found SIMPLE effects.

Rickles was unimpressed.

“You follow what I’m saying, Guy? There are TOO-MANY-EFFECTS. There’s too much going on in the data.”

“I don’t see how that’s possible,” I said. “Keith, Maria, and Lakshmi each spent weeks on this data and found nothing.”

“That,” said Rickles, “is because Keith, Maria, and Lakshmi never thought to apply the Epistocene Zulu transform to the data.”

The Epistocene Zulu transform! It made perfect sense when you thought about it; so why hadn’t I ever thought about it? Who was Rickles cribbing analysis notes from?

“Pull up the data,” I said excitedly. “I want to see what you’re talking about.”

“Alright, alright. Lunch hours are over now anyway.”

He grudgingly clicked on the little X on his browser. Then he pulled up a spreadsheet that must have had a million columns in it. I don’t know where they’d all come from; it had only had sixteen thousand or so when I’d had the hard drives delivered to his office.

“Here,” said Rickles, showing me the output of the Pear-sampled Tea test. “There’s the A-trax, and there’s its Nuffton index, and there’s the Zimming Range. Look at that effect. It’s bigger than the zifflon correlation Yehudah’s group reported in Nature last year.”

“Impressive,” I said, trying to look calm and collected. But in my head, I was already trying to figure out how I’d ask the department chair for a raise once this finding was published. Each point on that Zimming Range is worth at least $500, I thought.

“Are there any secondary analyses we could publish alongside that,” I asked.

“Oh, I don’t think you want to publish that,” Rickles laughed.

“Why the hell not? It could be big! You just said yourself it was a giant effect!”

“Oh sure. It’s a big effect. But I don’t believe it for one second.”

“Why not? What’s not to like? This finding make’s Yehudah’s paper look like a corn dog!”

I recognized, in the course of uttering those words, that they did not constitute the finest simile ever produced.

“Well, there are two massive outliers, for one. If you eliminate them, the effect is much smaller. And if you take into consideration the Gupta skew because the data were collected with the old reverberator, there’s nothing left at all.”

“Okay, fine,” I muttered. “Is there anything else in the data?”

“Sure, tons of things. Like, for example, there’s a statistically significant gamma reduction.”

“A gamma reduction? Are you sure? Or do you mean beta,” I asked.

“Definitely gamma,” said Rickles. “There’s nothing in the betas, deltas, or thetas. I checked.”

“Okay. That sounds potentially interesting and publishable. But I bet you’re going to tell me why we shouldn’t believe that result, either, right?”

“Well,” said Rickles, looking a bit self-conscious, “it’s just that it’s a pretty fine-grained analysis; you’re not really leaving a lot of observations when you slice it up that thin. And the weird thing about the gamma reduction is that it is essentially tantamount to accepting a null effect; this was Jayaraman’s point in that article in Statistica Splenda last month.”

“Sure, the Gerryman article, right. I read that. Forget the gamma reduction. What else?”

“There are quite a few schweizels,” Rickles offered, twisting the cap off a beer that had appeared out of the minibar under his desk.

I looked at him suspiciously. I suspected it was a trap; Rickels knew how much I loved Schweizel units. But I still couldn’t resist. I had to know.

“How many schweizels are there,” I asked, my hand clutching at the back of a nearby chair to help keep me steady.

“Fourteen,” Rickles said matter-of-factedly.

“Fourteen!” I gasped. “That’s a lot of schweizels!”

“It’s not bad,” said Rickles. “But the problem is, if you look at the B-trax, they also have a lot of schweizels. Seventeen of them, actually.”

“Seventeen schweizels!” I exclaimed. “That’s impossible! How can there be so many Schweizel units in one dataset!”

“I’m not sure. But… I can tell you that if you normalize the variables based on the Smith-Gill ratio, the effect goes away completely.”

There it was; the sound of the other shoe dropping. My heart gave a little cough–not unlike the sound your car engine makes in the morning when it’s cold and it wants you to stop provoking it and go back to bed. It was aggravating, but I understood what Rickles was saying. You couldn’t really say much about the Zimming Range unless your schweizel count was properly weighted. Still, I didn’t want to just give up on the schweizels entirely. I’d spent too much of my career delicately massaging schweizels to give up without one last tug.

“Maybe we can just say that the A-trax/Nuffton relationship is non-linear?” I suggested.

“Non-linear?” Rickles snorted. “Only if by non-linear you mean non-real! If it doesn’t survive Smith-Gill, it’s not worth reporting!”

I grudgingly conceded the point.

“What about the zifflons? Have you looked at them at all? It wouldn’t be so novel given Yehudah’s work, but we might still be able to get it into some place like Acta Ziffletica if there was an effect…”

“Tried it. There isn’t really any A-trax influence on zifflons. Or a B-trax effect, for that matter. There is a modest effect if you generate the Mish component for all the trax combined and look only at that. But that’s a lot of trax, and we’re not correcting for multiple Mishing, so I don’t really trust it…”

I saw that point too, and was now nearing despondency. Rickles had shot down all my best ideas one after the other. I wondered how I’d convince the department chair to let me keep my job.

Then it came to me in a near-blinding flash of insight. Near blinding, because I smashed my forehead on the overhead chandelier jumping out of my chair. An inch lower, and I’d have lost both eyes.

“We need to get that chandelier replaced,” I said, clutching my head in my hands. “It has no business hanging around in an office like this.”

“We need to get it replaced,” Rickles agreed. “I’ll do it tomorrow during my lunch hours.”

I knew that meant the chandelier would be there forever–or at least as long as Rickles inhabited the office.

“Have you tried counting the Dunams,” I suggested, rubbing my forehead delicately and getting back to my brilliant idea.

“No,” he said, leaning forward in his chair slightly. “I didn’t count Dunams.”

Ah-hah! I thought to myself. Not so smart are we now! The old boy’s still got some tricks up his sleeve.

“I think you should count the Dunams,” I offered sagely. “That always works for me. I do believe it might shed some light on this problem.”

“Well…” said Rickles, shaking his head slightly, “maaaaaybe. But Li published a paper in Psykometrika last year showing that Dunam counting is just a special case of Klein’s occidental protrusion method. And Klein’s method is more robust to violations of normality. So I used that. But I don’t really know how to interpret the results, because the residual is negative.”

I really had no idea either. I’d never come across a negative Dunam residual, and I’d never even heard of occidental protrusion. As far as I was concerned, it sounded like a made-up method.

“Okay,” I said, sinking back into my chair, ready to give up. “You’re right. This data… I don’t know. I don’t know what it means.”

I should have expected it, really; it was, after all, the dataset from hell. I was pretty sure my old RA had taken a quick jaunt through purgatory every morning before settling into the bench to run some experiments.

“I told you so,” said Rickles, putting his feet up on the desk and handing me a beer I didn’t ask for. “But don’t worry about it too much. I’m sure we’ll figure it out eventually. We probably just haven’t picked the right transformation yet. There’s Nordstrom, El-Kabir, inverse Zulu…”

He turned to his laptop and double-clicked an icon on the desktop that said “YouTube”.

“…or maybe you can just give the data to your new graduate student when she starts in a couple of weeks,” he said as an afterthought.

In the background, a video of a chimp and a puppy driving a Jeep started playing on a discolored laptop screen.

I mulled it over. Should I give the data to Josephine? Well, why not? She couldn’t really do any worse with it, and it would be a good way to break her will quickly.

“That’s not a bad idea, Rickles,” I said. “In fact, I think it might be the best idea you’ve had all week. Boy, that chimp is a really aggressive driver. Don’t drive angry, chimp! You’ll have an accid–ouch, that can’t be good.”

The

perils of digging too deep

Dr. Rickles the postdoc looked a bit startled when I walked into his office. He was eating a cheese sandwich and watching a chimp on a motorbike on his laptop screen.
“YouTube again?” I asked.
“Yes,” he said. “It’s lunch.”
“It’s 2:30 pm,” I said, pointing to my watch.
“Still my lunch hours.”
Lunch hours for Rickles were anywhere from 11 am to 4 pm. It depended on exactly when you walked in on him doing something he wasn’t supposed to; that was the event that marked the onset of Lunch.
“Fair enough,” I said. “I just stopped by to see how things were going.”
“Oh, quite well.” said Rickles. “Things are going well. I just found a video of a chimp and a squirrel riding a motorbike together. They aren’t even wearing helmets! I’ll send you the link.”
“Please don’t. I don’t like squirrels. But I meant with work. How’s the data looking.”
He shot me a pained look, like I’d just caught him stealing video game money from his grandmother.
“The data are TERRIBLE,” he said in all capital letters.
I wasn’t terribly surprised at that revelation; I’d handed Rickles the dataset only three days prior, taking care not to  tell him it was the dataset from hell. Rickles was the fourth or fifth person in the line of succession; the data had been handed down from postdoc to graduate student to postdoc for several years now. Everyone in the lab wanted to take a crack at it when they first heard about it, and no one in the lab wanted anything to do with it once they’d taken a peek. I’d given it to Rickles in part to teach him a lesson; he’d been in the lab for several weeks now and somehow still seemed happy and self-assured.
“Haven’t found anything interesting yet?” I asked. “I thought maybe if you ran the Flimflan test on the A-trax, you might get an effect. Or maybe if you jimmied the cryptos on the Borgatron…”
“No, no,” Rickles interrupted, waved me off. “The problem isn’t that there’s nothing interesting in the data; it’s that there’s too MUCH stuff. There are too MANY results. The story is too COMPLEX.”
That didn’t compute for me, so I just stared at him blankly. No one ever found COMPLEX effects in my lab. We usually stopped once we found SIMPLE effects.
Rickles was unimpressed.
“You follow what I’m saying, Guy? There are TOO-MANY-EFFECTS. There’s too much going on in the data.”
“I don’t see how that’s possible,” I said. “Keith, Maria, and Lakshmi each spent weeks on this data and found *nothing*.”
“That,” said Rickles, “is because Keith, Maria, and Lakshmi never thought to apply the Epistocene Zulu transform to the data.”
The Epistocene Zulu transform! It made perfect sense when you thought about it; so why hadn’t I ever thought about it? Who was Rickles cribbing analysis notes from?
“Pull up the data,” I said excitedly. “I want to see what you’re talking about.”
“Alright, alright. Lunch hours are over now anyway.”
He grudgingly clicked on the little X on his browser. Then he pulled up a spreadsheet that must have had a million columns in it. I don’t know where they’d all come from; it had only had sixteen thousand or so when I’d had the hard drives delivered to his office.
“Here,” said Rickles, showing me the output of the Pear-sampled Tea test. “There’s the A-trax, and there’s its Nuffton index, and there’s the Zimming Range. Look at that effect. It’s bigger than the zifflon correlation Yehudah’s group reported in Nature last year.”
“Impressive,” I said, trying to look calm and collected. But in my head, I was already trying to figure out how I’d ask the department chair for a raise once this finding was published. *Each point on that Zimming Range is worth at least $500*, I thought.
“Are there any secondary analyses we could publish alongside that,” I asked.
“Oh, I don’t think you want to publish *that*,” Rickles laughed.
“Why the hell not? It could be big! You just said yourself it was a giant effect!”
“Oh *sure*. It’s a big effect. But I don’t believe it for one second.”
“Why not? What’s not to like? This finding make’s Yehudah’s paper look like a corn dog!”
I recognized, in the course of uttering those words, that they did not constitute the finest simile ever.
“Well, there are two massive outliers, for one. If you eliminate them, the effect is much smaller. And if you take into consideration the Gupta skew because the data were collected with the old reverberator, there’s nothing left at all.”
“Okay, fine,” I muttered. “Is there anything else in the data?”
“Sure, tons of things. Like, for example, there’s a statistically significant Gamma reduction.”
“A gamma reduction? Are you sure? Or do you mean Beta,” I asked.
“Definitely gamma,” said Rickles. “There’s nothing in the betas, deltas, or thetas. I looked.”
“Okay. That sounds potentially interesting and publishable. But I bet you’re going to tell me why we shouldn’t believe that result, either, right?”
“Well,” said Rickles, looking a bit self-conscious, “it’s just that it’s a pretty fine-grained analysis; you’re not really leaving a lot of observations when you slice it up that thin. And the weird thing about the gamma reduction is that it is essentially tantamount to accepting a null effect; this was Jayaraman’s point in that article in *Statistica Splenda* last month.”
“Sure, the Gerryman article, right. Okay. Forget the gamma reduction. What else?”
“There are quite a few Schweizels,” Rickles offered, twisting the cap off a beer that had appeared out of the minibar under his desk.
I looked at him suspiciously. I suspected it was a trap; Rickels knew how much I loved Schweizel units. But I still couldn’t resist. I had to know.
“How many Schweizels are there,” I asked, my hand clutching at the back of a nearby chair to help me stay upright.
“Fourteen,” Rickles said matter-of-factedly.
“Fourteen!” I gasped. “That’s a lot of Schweizels!”
“It’s not bad,” said Rickles. “But the problem is, if you look at the B-trax, they also have a lot of Schweizels. Seventeen of them, actually.”
“Seventeen Schweizels!” I exclaimed. “That’s impossible! How can there be so many Schweizel units in one dataset!”
“I’m not sure. But… I can tell you that if you normalize the variables based on the Smith-Gill ratio, the effect goes away completely.”
There it was; the sound of the other shoe dropping. My heart gave a little cough–not unlike the sound your car engine makes in the morning when it’s cold and it wants you to go back to bed and stop stressing it out. It was aggravating, but I understood what Rickles was saying. You couldn’t really say much about the Zimming Range unless your Schweizel count was properly weighted. Still, I didn’t want to just give up on the Schweizels entirely.
“Maybe we can just say that the A-trax/Nuffton relationship is non-linear,” I proposed.
“Non-linear?” Rickles snorted. “Only if by non-linear you mean non-real! If it doesn’t survive Smith-Gill, it’s not worth reporting!”
I grudgingly conceded the point.
“What about the zifflons? Have you looked at them at all? It wouldn’t be so novel given Yehudah’s work, but we might still be able to get it into some place like *Acta Ziffletica* if there was an effect…”
“Tried it. There isn’t really any A-trax influence on zifflons. Or a B-trax effect, for that matter. There *is* a modest effect if you generate the Mish component for all the trax combined and look only at that. But that’s a lot of trax, and we’re not correcting for multiple Mishing, so I don’t really trust it…”
I saw that point too, and was now nearing despondency. Rickles had shot down all my best ideas one after the other. What else was left?
Then it came to me in a near-blinding flash of insight. *Near* blinding, because I smashed my forehead on the overhead chandelier jumping out of my chair. An inch lower, and I’d have lost both eyes.
“We need to get that chandelier replaced,” I said, clutching my head in my hands. “It has no business hanging around in an office like this.”
“We need to get it replaced,” Rickles agreed. “I’ll do it tomorrow during my lunch hours.”
I knew that meant the chandelier would be there forever–or at least as long as Rickles inhabited the office.
“Have you tried counting the Dunams,” I suggested, rubbing my forehead delicately and getting back to my brilliant idea.
“No,” he said, leaning forward in his chair slightly. “I didn’t count Dunams.”
Ah-hah! I thought to myself. Not so smart are we now! The old boy’s still got some tricks up his sleeve.
“I think you should count the Dunams,” I offered sagely. “That always works for me. I do believe it might shed some light on this problem.”
“Well…” said Rickles, shaking his head slightly, “maaaaaybe. But Li published a paper in Psychometrika last year showing that Dunam counting is just a special case of Klein’s occidental protrusion method. And Klein’s method is more robust to violations of normality. So I used that. But I don’t really know how to interpret the results, because the residual is *negative*.”
I really had no idea either. I’d never come across a negative Dunam residual, and I’d never even heard of occidental protrusion. As far as I was concerned, it sounded like a made-up method.
“Okay,” I said, sinking back into my chair, ready to give up. “You’re right. This data… I don’t know. I don’t know what it means.” I should have expected it, really; it was, after all, the dataset from hell. I was pretty sure my old RA had collected it after taking a quick jaunt through purgatory every morning.
“I told you so,” said Rickles, putting his feet up on the desk and handing me a beer I didn’t ask for. “But don’t worry about it too much. I’m sure we’ll figure it out eventually. We probably just haven’t picked the right transformation yet.”
He turned to his laptop and double-clicked an icon on the desktop that said “YouTube”.
“Maybe you can give the data to your new graduate student when she starts in a couple of weeks,” he said as an afterthought.
In the background, a video of a chimp and a puppy driving a Jeep started playing on a discolored laptop screen.
I mulled it over. Should I give the data to Josephine? Well, why not? She couldn’t really do any *worse* with it, and it *would* be a good way to break her will in a hurry.
“That’s not a bad idea, Rickles,” I said. “In fact, I think it might be the best idea you’ve had all week. Boy, that chimp is a really aggressive driver. Don’t drive angry, chimp! You’ll have an accid–ouch, that can’t be good.”

undergraduates are WEIRD

This month’s issue of Nature Neuroscience contains an editorial lambasting the excessive reliance of psychologists on undergraduate college samples, which, it turns out, are pretty unrepresentative of humanity at large. The impetus for the editorial is a mammoth in-press review of cross-cultural studies by Joseph Henrich and colleagues, which, the authors suggest, collectively indicate that “samples drawn from Western, Educated, Industrialized, Rich and Democratic (WEIRD) societies … are among the least representative populations one could find for generalizing about humans.” I’ve only skimmed the article, but aside from the clever acronym, you could do a lot worse than these (rather graphic) opening paragraphs:

In the tropical forests of New Guinea the Etoro believe that for a boy to achieve manhood he must ingest the semen of his elders. This is accomplished through ritualized rites of passage that require young male initiates to fellate a senior member (Herdt, 1984; Kelley, 1980). In contrast, the nearby Kaluli maintain that  male initiation is only properly done by ritually delivering the semen through the initiate’s anus, not his mouth. The Etoro revile these Kaluli practices, finding them disgusting. To become a man in these societies, and eventually take a wife, every boy undergoes these initiations. Such boy-inseminating practices, which  are enmeshed in rich systems of meaning and imbued with local cultural values, were not uncommon among the traditional societies of Melanesia and Aboriginal Australia (Herdt, 1993), as well as in Ancient Greece and Tokugawa Japan.

Such in-depth studies of seemingly “exotic“ societies, historically the province of anthropology, are crucial for understanding human behavioral and psychological variation. However, this paper is not about these peoples. It’s about a truly unusual group: people from Western, Educated, Industrialized, Rich, and Democratic (WEIRD) societies. In particular, it’s about the Western, and more specifically American, undergraduates who form the bulk of the database in the experimental branches of psychology, cognitive science, and economics, as well as allied fields (hereafter collectively labeled the “behavioral sciences“). Given that scientific knowledge about human psychology is largely based on findings from this subpopulation, we ask just how representative are these typical subjects in light of the available comparative database. How justified are researchers in assuming a species-level generality for their findings? Here, we review the evidence regarding how WEIRD people compare to other
populations.

Anyway, it looks like a good paper. Based on a cursory read, the conclusions the authors draw seem pretty reasonable, if a bit strong. I think most researchers do already recognize that our dependence on undergraduates is unhealthy in many respects; it’s just that it’s difficult to break the habit, because the alternative is to spend a lot more time and money chasing down participants (and there are limits to that too; it just isn’t feasible for most researchers to conduct research with Etoro populations in New Guinea). Then again, just because it’s hard to do science the right way doesn’t really make it OK to do it the wrong way. So, to the extent that we care about our results generalizing across the entire human species (which, in many cases, we don’t), we should probably be investing more energy in weaning ourselves off undergraduates and trying to recruit more diverse samples.

functional MRI and the many varieties of reliability

Craig Bennett and Mike Miller have a new paper on the reliability of fMRI. It’s a nice review that I think most people who work with fMRI will want to read. Bennett and Miller discuss a number of issues related to reliability, including why we should care about the reliability of fMRI, what factors influence reliability, how to obtain estimates of fMRI reliability, and what previous studies suggest about the reliability of fMRI. Their bottom line is that the reliability of fMRI often leaves something to be desired:

One thing is abundantly clear: fMRI is an effective research tool that has opened broad new horizons of investigation to scientists around the world. However, the results from fMRI research may be somewhat less reliable than many researchers implicitly believe. While it may be frustrating to know that fMRI results are not perfectly replicable, it is beneficial to take a longer-term view regarding the scientific impact of these studies. In neuroimaging, as in other scientific fields, errors will be made and some results will not replicate.

I think this is a wholly appropriate conclusion, and strongly recommend reading the entire article. Because there’s already a nice write-up of the paper over at Mind Hacks, I’ll content myself to adding a number of points to B&M’s discussion (I talk about some of these same issues in a chapter I wrote with Todd Braver).

First, even though I agree enthusiastically with the gist of B&M’s conclusion, it’s worth noting that, strictly speaking, there’s actually no such thing as “the reliability of fMRI”. Reliability isn’t a property of a technique or instrument, it’s a property of a specific measurement. Because every measurement is made under slightly different conditions, reliability will inevitably vary on a case-by-case basis. But since it’s not really practical (or even possible) to estimate reliability for every single analysis, researchers take necessary short-cuts. The standard in the psychometric literature is to establish reliability on a per-measure (not per-method!) basis, so long as conditions don’t vary too dramatically across samples. For example, once someone “validates” a given self-report measure, it’s generally taken for granted that that measure is “reliable”, and most people feel comfortable administering it to new samples without having to go to the trouble of estimating reliability themselves. That’s a perfectly reasonable approach, but the critical point is that it’s done on a relatively specific basis. Supposing you made up a new self-report measure of depression from a set of items you cobbled together yourself, you wouldn’t be entitled to conclude that your measure was reliable simply because some other self-report measure of depression had already been psychometrically validated. You’d be using an entirely new set of items, so you’d have to go to the trouble of validating your instrument anew.

By the same token, the reliability of any given fMRI measurement is going to fluctuate wildly depending on the task used, the timing of events, and many other factors. That’s not just because some estimates of reliability are better than others; it’s because there just isn’t a fact of the matter about what the “true” reliability of fMRI is. Rather, there are facts about how reliable fMRI is for specific types of tasks with specific acquisition parameters and preprocessing streams in specific scanners, and so on (which can then be summarized by talking about the general distribution of fMRI reliabilities). B&M are well aware of this point, and discuss it in some detail, but I think it’s worth emphasizing that when they say that “the results from fMRI research may be somewhat less reliable than many researchers implicitly believe,” what they mean isn’t that the “true” reliability of fMRI is likely to be around .5; rather, it’s that if you look at reliability estimates across a bunch of different studies and analyses, the estimated reliability is often low. But it’s not really possible to generalize from this overall estimate to any particular study; ultimately, if you want to know whether your data were measured reliably, you need to quantify that yourself. So the take-away message shouldn’t be that fMRI is an inherently unreliable method (and I really hope that isn’t how B&M’s findings get reported by the mainstream media should they get picked up), but rather, that there’s a very good chance that the reliability of fMRI in any given situation is not particularly high. It’s a subtle difference, but an important one.

Second, there’s a common misconception that reliability estimates impose an upper bound on the true detectable effect size. B&M make this point in their review, Vul et al made it in their “voodoo correlations”” paper, and in fact, I’ve made it myself before. But it’s actually not quite correct. It’s true that, for any given test, the true reliability of the variables involved limits the potential size of the true effect. But there are many different types of reliability, and most will generally only be appropriate and informative for a subset of statistical procedures. Virtually all types of reliability estimate will underestimate the true reliability in some cases and overestimate it in others. And in extreme cases, there may be close to zero relationship between the estimate and the truth.

To see this, take the following example, which focuses on internal consistency. Suppose you have two completely uncorrelated items, and you decide to administer them together as a single scale by simply summing up their scores. For example, let’s say you have an item assessing shoelace-tying ability, and another assessing how well people like the color blue, and you decide to create a shoelace-tying-and-blue-preferring measure. Now, this measure is clearly nonsensical, in that it’s unlikely to predict anything you’d ever care about. More important for our purposes, its internal consistency would be zero, because its items are (by hypothesis) uncorrelated, so it’s not measuring anything coherent. But that doesn’t mean the measure is unreliable! So long as the constituent items are each individually measured reliably, the true reliability of the total score could potentially be quite high, and even perfect. In other words, if I can measure your shoelace-tying ability and your blueness-liking with perfect reliability, then by definition, I can measure any linear combination of those two things with perfect reliability as well. The result wouldn’t mean anything, and the measure would have no validity, but from a reliability standpoint, it’d be impeccable. This problem of underestimating reliability when items are heterogeneous has been discussed in the psychometric literature for at least 70 years, and yet you still very commonly see people do questionable things like “correcting for attenuation” based on dubious internal consistency estimates.

In their review, B&M mostly focus on test-retest reliability rather than internal consistency, but the same general point applies. Test-retest reliability is the degree to which people’s scores on some variable are consistent across multiple testing occasions. The intuition is that, if the rank-ordering of scores varies substantially across occasions (e.g., if the people who show the highest activation of visual cortex at Time 1 aren’t the same ones who show the highest activation at Time 2), the measurement must not have been reliable, so you can’t trust any effects that are larger than the estimated test-retest reliability coefficient. The problem with this intuition is that there can be any number of systematic yet session-specific influences on a person’s score on some variable (e.g., activation level). For example, let’s say you’re doing a study looking at the relation between performance on a difficult working memory task and frontoparietal activation during the same task. Suppose you do the exact same experiment with the same subjects on two separate occasions three weeks apart, and it turns out that the correlation between DLPFC activation across the two occasions is only .3. A simplistic view would be that this means that the reliability of DLPFC activation is only .3, so you couldn’t possibly detect any correlations between performance level and activation greater than .3 in DLPFC. But that’s simply not true. It could, for example, be that the DLPFC response during WM performance is perfectly reliable, but is heavily dependent on session-specific factors such as baseline fatigue levels, motivation, and so on. In other words, there might be a very strong and perfectly “real” correlation between WM performance and DLPFC activation on each of the two testing occasions, even though there’s very little consistency across the two occasions. Test-retest reliability estimates only tell you how much of the signal is reliably due to temporally stable variables, and not how much of the signal is reliable, period.

The general point is that you can’t just report any estimate of reliability that you like (or that’s easy to calculate) and assume that tells you anything meaningful about the likelihood of your analyses succeeding. You have to think hard about exactly what kind of reliability you care about, and then come up with an estimate to match that. There’s a reasonable argument to be made that most of the estimates of fMRI reliability reported to date are actually not all that relevant to many people’s analyses, because the majority of reliability analyses have focused on test-retest reliability, which is only an appropriate way to estimate reliability if you’re trying to relate fMRI activation to stable trait measures (e.g., personality or cognitive ability). If you’re interested in relating in-scanner task performance or state-dependent variables (e.g., mood) to brain activation (arguably the more common approach), or if you’re conducting within-subject analyses that focus on comparisons between conditions, using test-retest reliability isn’t particularly informative, and you really need to focus on other types of reliability (or reproducibility).

Third, and related to the above point, between-subject and within-subject reliability are often in statistical tension with one another. B&M don’t talk about this, as far as I can tell, but it’s an important point to remember when designing studies and/or conducting analyses. Essentially, the issue is that what counts as error depends on what effects you’re interested in. If you’re interested in individual differences, it’s within-subject variance that counts as error, so you want to minimize that. Conversely, if you’re interested in within-subject effects (the norm in fMRI), you want to minimize between-subject variance. But you generally can’t do both of these at the same time. If you use a very “strong” experimental manipulation (i.e., a task that produces a very large difference between conditions for virtually all subjects), you’re going to reduce the variability between individuals, and you may very well end up with very low test-retest reliability estimates. And that would actually be a good thing! Conversely, if you use a “weak” experimental manipulation, you might get no mean effect at all, because there’ll be much more variability between individuals. There’s no right or wrong here; the trick is to pick a design that matches the focus of your study. In the context of reliability, the essential point is that if all you’re interested in is the contrast between high and low working memory load, it shouldn’t necessarily bother you if someone tells you that the test-retest reliability of induced activation in your study is close to zero. Conversely, if you care about individual differences, it shouldn’t worry you if activations aren’t reproducible across studies at the group level. In some ways, those are actual the ideal situations for each of those two types of studies.

Lastly, B&M raise a question as to what level of reliability we should consider “acceptable” for fMRI research:

There is no consensus value regarding what constitutes an acceptable level of reliability in fMRI. Is an ICC value of 0.50 enough? Should studies be required to achieve an ICC of 0.70? All of the studies in the review simply reported what the reliability values were. Few studies proposed any kind of criteria to be considered a “˜reliable’ result. Cicchetti and Sparrow did propose some qualitative descriptions of data based on the ICC-derived reliability of results (1981). They proposed that results with an ICC above 0.75 be considered “˜excellent’, results between 0.59 and 0.75 be considered “˜good’, results between .40 and .58 be considered “˜fair’, and results lower than 0.40 be considered “˜poor’. More specifically to neuroimaging, Eaton et al. (2008) used a threshold of ICC > 0.4 as the mask value for their study while Aron et al. (2006) used an ICC cutoff of ICC > 0.5 as the mask value.

On this point, I don’t really see any reason to depart from psychometric convention just because we’re using fMRI rather than some other technique. Conventionally, reliability estimates of around .8 (or maybe .7, if you’re feeling generous) are considered adequate. Any lower and you start to run into problems, because effect sizes will shrivel up. So I think we should be striving to attain the same levels of reliability with fMRI as with any other measure. If it turns out that that’s not possible, we’ll have to live with that, but I don’t think the solution is to conclude that reliability estimates on the order of .5 are ok “for fMRI” (I’m not saying that’s what B&M say, just that that’s what we should be careful not to conclude). Rather, we should just accept that the odds of detecting certain kinds of effects with fMRI are probably going to be lower than with other techniques. And maybe we should minimize the use of fMRI for those types of analyses where reliability is generally not so good (e.g., using brain activation to predict trait variables over long intervals).

I hasten to point out that none of this should be taken as a criticism of B&M’s paper; I think all of these points complement B&M’s discussion, and don’t detract in any way from its overall importance. Reliability is a big topic, and there’s no way Bennett and Miller could say everything there is to be said about it in one paper. I think they’ve done the field of cognitive neuroscience an important service by raising awareness and providing an accessible overview of some of the issues surrounding reliability, and it’s certainly a paper that’s going on my “essential readings in fMRI methods” list.

ResearchBlogging.org
Bennett, C. M., & Miller, M. B. (2010). How reliable are the results from functional magnetic resonance imaging? Annals of the New York Academy of Sciences

specificity statistics for ROI analyses: a simple proposal

The brain is a big place. In the context of fMRI analysis, what that bigness means is that a typical 3D image of the brain might contain anywhere from 50,000 – 200,000 distinct voxels (3D pixels). Any of those voxels could theoretically show meaningful activation in relation to some contrast of interest, so the only way to be sure that you haven’t overlooked potentially interesting activations is to literally test every voxel (or, given some parcellation algorithm, every region).

Unfortunately, the problem that approach raises–which I’ve discussed in more detail here–is the familiar one of multiple comparisons: If you’re going to test 100,000 locations, it’s not really fair to test each one at the conventional level of p < .05, because on average, you’ll get about 5,000 statistically significant results just by chance that way. So you need to do something to correct for the fact that you’re running thousands of tests. The most common approach is to simply make the threshold for significance more conservative–for example, by testing at p < .0001 instead of p < .05, or by using some combination of intensity and cluster extent thresholds (e.g., you look for 20 contiguous voxels that are all significant at, say, p < .001) that’s supposed to guarantee a cluster-wise error rate of .05.

There is, however, a natural tension between false positives and false negatives: When you make your analysis more conservative, you let fewer false positives through the filter, but you also keep more of the true positives out. A lot of fMRI analysis really just boils down to walking a very thin line between running overconservative analyses that can’t detect anything but the most monstrous effects, and running overly liberal analyses that lack any real ability to distinguish meaningful signals from noise. One very common approach that fMRI researchers have adopted in an effort to optimize this balance is to use complementary hypothesis-driven and whole-brain analyses. The idea is that you’re basically carving the brain up into two separate search spaces: One small space for which you have a priori hypotheses that can be tested using a small number of statistical comparisons, and one much larger space (containing everything but the a priori space) where you continue to use a much more conservative threshold.

For example, if I believe that there’s a very specific chunk of right inferotemporal cortex that’s specialized for detecting clown faces, I can focus my hypothesis-testing on that particular region, without having to pretend that all voxels are created equal. So I delineate the boundaries of a CRC (Clown Representation Cortex) region-of-interest (ROI) based on some prior criteria (e.g., anatomy, or CRC activation in previous studies), and then I can run a single test at p < .05 to test my hypothesis, no correction needed. But to ensure that I don’t miss out on potentially important clown-related activation elsewhere in the brain, I also go ahead and run an additional whole-brain analysis that’s fully corrected for multiple comparisons. By coupling these two analyses, I hopefully get the best of both worlds. That is, I combine one approach (the ROI analysis) that maximizes power to test a priori hypotheses at the cost of an inability to detect effects in unexpected places with another approach (the whole-brain analysis) that has a much more limited capacity to detect effects in both expected and unexpected locations.

This two-pronged strategy is generally a pretty successful one, and I’d go so far as to say that a very large minority, if not an outright majority, of fMRI studies currently use it. Used wisely, I think it’s really an invaluable strategy. There is, however, one fairly serious and largely unappreciated problem associated with the incautious application of this approach. It has to do with claims about the specificity of activation that often tend to accompany studies that use a complementary ROI/whole-brain strategy. Specifically, a pretty common pattern is for researchers to (a) confirm their theoretical predictions by successfully detecting activation in one or more a priori ROIs; (b) identify few if any whole-brain activations; and consequently, (c) conclude that not only were the theoretical predictions confirmed, but that the hypothesized effects in the a priori ROIs were spatially selective, because a complementary whole-brain analysis didn’t turn up much (if anything). Or, to put it in less formal terms, not only were we right, we were really right! There isn’t any other part of the brain that shows the effect we hypothesized we’d see in our a priori ROI!

The problem with this type of inference is that there’s usually a massive discrepancy in the level of power available to detect effects in a priori ROIs versus the rest of the brain. If you search at p < .05 within some predetermined space, but at only p < .0001 everywhere else, you’re naturally going to detect results at a much lower rate everywhere else. But that’s not necessarily because there wasn’t just as much to look at everywhere else; it could just be because you didn’t look very carefully. By way of analogy, if you’re out picking berries in the forest, and you decide to spend half your time on just one bush that (from a distance) seemed particularly berry-full, and the other half of your time divided between the other 40 bushes in the area, you’re not really entitled to conclude that you picked the best bush all along simply because you came away with a relatively full basket. Had you done a better job checking out the other bushes, you might well have found some that were even better, and then you’d have come away carrying two baskets full of delicious, sweet, sweet berries.

Now, in an ideal world, we’d solve this problem by simply going around and carefully inspecting all the berry bushes, until we were berry, berry sure really convinced that we’d found all of the best bushes. Unfortunately, we can’t do that, because we’re out here collecting berries on our lunch break, and the boss isn’t paying us to dick around in the woods. Or, to return to fMRI World, we simply can’t carefully inspect every single voxel (say, by testing it at p < .05), because then we’re right back in mega-false-positive-land, which we’ve already established as a totally boring place we want to avoid at all costs.

Since an optimal solution isn’t likely, the next best thing is to figure out what we can do to guard against careless overinterpretation. Here I think there’s actually a very simple, and relatively elegant, solution. What I’ve suggested when I’ve given recent talks on this topic is that we mandate (or at least, encourage) the use of what you could call a specificity statistic (SS). The SS is a very simple measure of how specific a given ROI-level finding is; it’s just the proportion of voxels that are statistically significant when tested at the same level as the ROI-level effects. In most cases, that’s going to be p < .05, so the SS will usually just be the proportion of all voxels anywhere in the brain that are activated at p < .05.

To see why this is useful, consider what could no longer happen: Researchers would no longer be able to (inadvertently) capitalize on the fact that the one or two regions they happened to define as a priori ROIs turned up significant effects when no other regions did in a whole-brain analysis. Suppose that someone reports a finding that negative emotion activates the amygdala in an ROI analysis, but doesn’t activate any other region in a whole-brain analysis. (While I’m pulling this particular example out of a hat here, I feel pretty confident that if you went and did a thorough literature review, you’d find at least three or four studies that have made this exact claim.) This is a case where the SS would come in really handy. Because if the SS is, say, 26% (i.e., about a quarter of all voxels in the brain are active at p < .05, even if none survive full correction for multiple comparisons), you would want to draw a very different conclusion than if it was just 4%. If fully a quarter of the brain were to show greater activation for a negative-minus-neutral emotion contrast, you wouldn’t want to conclude that the amygdala was critically involved in negative emotion; a better interpretation would be that the researchers in question just happened to define an a priori region that fell within the right quarter of the brain. Perhaps all that’s happening is that negative emotion elicits a general increase in attention, and much of the brain (including, but by no means limited to, the amygdala) tends to increase activation correspondingly. So as a reviewer and reader, you’d want to know how specific the reported amygdala activation really is*. But in the vast majority of papers, you currently have no way of telling (and the researchers probably don’t even know the answer themselves!).

The principal beauty of this statistic lies in its simplicity: It’s easy to understand, easy to calculate, and easy to report. Ideally, researchers would report the SS any time ROI analyses are involved, and would do it for every reported contrast. But at minimum, I think we should all encourage each other (and ourselves) to report such a statistic any time we’re making a specificity claim about ROI-based results. In other words,if you want to argue that a particular cognitive function is relatively localized to the ROI(s) you happened to select, you should be required to show that there aren’t that many other voxels (or regions) that show the same effect when tested at the liberal threshold you used for the ROI analysis. There shouldn’t be an excuse for not doing this; it’s a very easy procedure for researchers to implement, and an even easier one for reviewers to demand.

* An alternative measure of specificity would be to report the percentile ranking of all of the voxels within the ROI mask relative to all other individual voxels. In the above example, you’d assign very different interpretations depending on whether the amygdala was in the 32nd or 87th percentile of all voxels, when ordered according to the strength of the effect for the negative – neutral contrast.