## trouble with biomarkers and press releases

The latest issue of the Journal of Neuroscience contains an interesting article by Ecker et al in which the authors attempted to classify people with autism spectrum disorder (ASD) and health controls based on their brain anatomy, and report achieving “a sensitivity and specificity of up to 90% and 80%, respectively.” Before unpacking what that means, and why you probably shouldn’t get too excited (about the clinical implications, at any rate; the science is pretty cool), here’s a snippet from the decidedly optimistic press release that accompanied the study:

“Scientists funded by the Medical Research Council (MRC) have developed a pioneering new method of diagnosing autism in adults. For the first time, a quick brain scan that takes just 15 minutes can identify adults with autism with over 90% accuracy. The method could lead to the screening for autism spectrum disorders in children in the future.”

If you think this sounds too good to be true, that’s because it is. Carl Heneghan explains why in an excellent article in the Guardian:

How the brain scans results are portrayed is one of the simplest mistakes in interpreting diagnostic test accuracy to make. What has happened is, the sensitivity has been taken to be the positive predictive value, which is what you want to know: if I have a positive test do I have the disease? Not, if I have the disease, do I have a positive test? It would help if the results included a measure called the likelihood ratio (LR), which is the likelihood that a given test result would be expected in a patient with the target disorder compared to the likelihood that the same result would be expected in a patient without that disorder. In this case the LR is 4.5. We’ve put up an article if you want to know more on how to calculate the LR.

In the general population the prevalence of autism is 1 in 100; the actual chances of having the disease are 4.5 times more likely given a positive test. This gives a positive predictive value of 4.5%; about 5 in every 100 with a positive test would have autism.

For those still feeling confused and not convinced, let’s think of 10,000 children. Of these 100 (1%) will have autism, 90 of these 100 would have a positive test, 10 are missed as they have a negative test: there’s the 90% reported accuracy by the media.

But what about the 9,900 who don’t have the disease? 7,920 of these will test negative (the specificity3 in the Ecker paper is 80%). But, the real worry though, is the numbers without the disease who test positive. This will be substantial: 1,980 of the 9,900 without the disease. This is what happens at very low prevalences, the numbers falsely misdiagnosed rockets. Alarmingly, of the 2,070 with a positive test, only 90 will have the disease, which is roughly 4.5%.

In other words, if you screened everyone in the population for autism, and assume the best about the classifier reported in the JNeuro article (e.g., that the sample of 20 ASD participants they used is perfectly representative of the broader ASD population, which seems unlikely), only about 1 in 20 people who receive a positive diagnosis would actually deserve one.

Ecker et al object to this characterization, and reply to Heneghan in the comments (through the MRC PR office):

Our test was never designed to screen the entire population of the UK. This is simply not practical in terms of costs and effort, and besides totallyÂ  unjustified- why would we screen everybody in the UK for autism if there is no evidence whatsoever that an individual is affected?. The same case applies to other diagnostic tests. Not every single individual in the UK is tested for HIV. Clearly this would be too costly and unnecessary. However, in the group of individuals that are test for the virus, we can be very confident that if the test is positive that means a patient is infected. The same goes for our approach.

Essentially, the argument is that, since people would presumably be sent for an MRI scan because they were already under consideration for an ASD diagnosis, and not at random, the false positive rate would in fact be much lower than 95%, and closer to the 20% reported in the article.

One response to this reply–which is in fact Heneghan’s response in the comments–is to point out that the pre-test probability of ASD would need to be pretty high already in order for the classifier to add much. For instance, even if fully 30% of people who were sent for a scan actually had ASD, the posterior probability of ASD given a positive result would still be only 66% (Heneghan’s numbers, which I haven’t checked). Heneghan nicely contrasts these results with the standard for HIV testing, which “reports sensitivity of 99.7% and specificity of 98.5% for enzyme immunoassay.” Clearly, we have a long way to go before doctors can order MRI-based tests for ASD and feel reasonably confident that a positive result is sufficient grounds for an ASD diagnosis.

Setting Heneghan’s concerns about base rates aside, there’s a more general issue that he doesn’t touch on. It’s one that’s not specific to this particular study, and applies to nearly all studies that attempt to develop “biomarkers” for existing disorders. The problem is that the sensitivity and specificity values that people report for their new diagnostic procedure in these types of studies generally aren’t the true parameters of the procedure. Rather, they’re the sensitivity and specificity under the assumption that the diagnostic procedures used to classify patients and controls in the first place are themselves correct. In other words, in order to believe the results, you have to assume that the researchers correctly classified the subjects into patient and control groups using other procedures. In cases where the gold standard test used to make the initial classification is known to have near 100% sensitivity and specificity (e.g., for the aforementioned HIV tests), one can reasonably ignore this concern. But when we’re talking about mental health disorders, where diagnoses are fuzzy and borderline cases abound, it’s very likely that the “gold standard” isn’t really all that great to begin with.

Concretely,Â  studies that attempt to develop biomarkers for mental health disorders face two substantial problems. One is that it’s extremely unlikely that the clinical diagnoses are ever perfect; after all, if they were perfect, there’d be little point in trying to develop other diagnostic procedures! In this particular case, the authors selected subjects into the ASD group based on standard clinical instruments and structured interviews. I don’t know that there are many clinicians who’d claim with a straight face that the current diagnostic criteria for ASD (and there are multiple sets to choose from!) are perfect. From my limited knowledge, the criteria for ASD seem to be even more controversial than those for most other mental health disorders (which is saying something, if you’ve been following the ongoing DSM-V saga). So really, the accuracy of the classifier in the present study, even if you put the best face on it and ignore the base rate issue Heneghan brings up, is undoubtedly south of the 90% sensitivity / 80% specificity the authors report. How much south, we just don’t know, because we don’t really have any independent, objective way to determine who “really” should get an ASD diagnosis and who shouldn’t (assuming you think it makes sense to make that kind of dichotomous distinction at all). But 90% accuracy is probably a pipe dream, if for no other reason than it’s hard to imagine that level of consensus about autism spectrum diagnoses.

The second problem is that, because the researchers are using the MRI-based classifier to predict the clinician-based diagnosis, it simply isn’t possible for the former to exceed the accuracy of the latter. That bears repeating, because it’s important: no matter how good the MRI-based classifier is, it can only be as good as the procedures used to make the original diagnosis, and no better. It cannot, by definition, make diagnoses that are any more accurate than the clinicians who screened the participants in the authors’ ASD sample. So when you see the press release say this:

For the first time, a quick brain scan that takes just 15 minutes can identify adults with autism with over 90% accuracy.

You should really read it as this:

The method relies on structural (MRI) brain scans and has an accuracy rate approaching that of conventional clinical diagnosis.

That’s not quite as exciting, obviously, but it’s more accurate.

To be fair, there’s something of a catch-22 here, in that the authors didn’t really have a choice about whether or not to diagnose the ASD group using conventional criteria. If they hadn’t, reviewers and other researchers would have complained that we can’t tell if the ASD group is really an ASD group, because they authors used non-standard criteria. Under the circumstances, they did the only thing they could do. But that doesn’t change the fact that it’s misleading to intimate, as the press release does, that the new procedure might be any better than the old ones. It can’t be, by definition.

Ultimately, if we want to develop brain-based diagnostic tools that are more accurate than conventional clinical diagnoses, we’re going to need to show that these tools are capable of predicting meaningful outcomes that clinician diagnoses can’t. This isn’t an impossible task, but it’s a very difficult one. One approach you could take, for instance, would be to compare the ability of clinician diagnosis and MRI-based diagnosis to predict functional outcomes among subjects at a later point in time. If you could show that MRI-based classification of subjects at an early age was a stronger predictor of receiving an ASD diagnosis later in life than conventional criteria, that would make a really strong case for using the former approach in the real world. Short of that type of demonstration though, the only reason I can imagine wanting to use a procedure that was developed by trying to duplicate the results of an existing procedure is in the event that the new procedure is substantially cheaper or more efficient than the old one. Meaning, it would be reasonable enough to say “well, look, we don’t do quite as well with this approach as we do with a full clinical evaluation, but at least this new approach costs much less.” Unfortunately, that’s not really true in this case, since the price of even a short MRI scan is generally going to outweigh that of a comprehensive evaluation by a psychiatrist or psychotherapist. And while it could theoretically be much faster to get an MRI scan than an appointment with a mental health professional, I suspect that that’s not generally going to be true in practice either.

Having said all that, I hasten to note that all this is really a critique of the MRC press release and subsequently lousy science reporting, and not of the science itself. I actually think the science itself is very cool (but the Neuroskeptic just wrote a great rundown of the methods and results, so there’s not much point in me describing them here). People have been doing really interesting work with pattern-based classifiers for several years now in the neuroimaging literature, but relatively few studies have applied this kind of technique to try and discriminate between different groups of individuals in a clinical setting. While I’m not really optimistic that the technique the authors introduce in this paper is going to change the way diagnosis happens any time soon (or at least, I’d argue that it shouldn’t), there’s no question that the general approach will be an important piece of future efforts to improve clinical diagnoses by integrating biological data with existing approaches. But that’s not going to happen overnight, and in the meantime, I think it’s pretty irresponsible of the MRC to be issuing press releases claiming that its researchers can diagnose autism in adults with 90% accuracy.

Ecker C, Marquand A, MourÃ£o-Miranda J, Johnston P, Daly EM, Brammer MJ, Maltezos S, Murphy CM, Robertson D, Williams SC, & Murphy DG (2010). Describing the brain in autism in five dimensions–magnetic resonance imaging-assisted diagnosis of autism spectrum disorder using a multiparameter classification approach. The Journal of neuroscience : the official journal of the Society for Neuroscience, 30 (32), 10612-23 PMID: 20702694

## 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.