[citation needed]

A new paper published online this week in the Journal of Cerebral Blood Flow & Metabolism this week discusses the infamous problem of circular analysis in fMRI research. The paper is aptly titled “Everything you never wanted to know about circular analysis, but were afraid to ask,” and is authored by several well-known biostatisticians and cognitive neuroscientists–to wit, Niko Kriegeskorte, Martin Lindquist, Tom Nichols, Russ Poldrack, and Ed Vul. The paper has an interesting format, and one that I really like: it’s set up as a series of fourteen questions related to circular analysis, and each author answers each question in 100 words or less.

I won’t bother going over the gist of the paper, because the Neuroskeptic already beat me to the punch in an excellent post a couple of days ago (actually, that’s how I found out about the paper); instead,  I’ll just give my own answers to the same set of questions raised in the paper. And since blog posts don’t have the same length constraints as NPG journals, I’m going to be characteristically long-winded and ignore the 100 word limit…

(1) Is circular analysis a problem in systems and cognitive neuroscience?

Yes, it’s a huge problem. That said, I think the term ‘circular’ is somewhat misleading here, because it has the connotation than an analysis is completely vacuous. Truly circular analyses–i.e., those where an initial analysis is performed, and the researchers then conduct a “follow-up” analysis that literally adds no new information–are relatively rare in fMRI research. Much more common are cases where there’s some dependency between two different analyses, but the second one still adds some novel information.

(2) How widespread are slight distortions and serious errors caused by circularity in the neuroscience literature?

I think Nichols sums it up nicely here:

TN: False positives due to circularity are minimal; biased estimates of effect size are common. False positives due to brushing off the multiple testing problem (e.g., ‘P<0.001 uncorrected’ and crossing your fingers) remain pervasive.

The only thing I’d add to this is that the bias in effect size estimates is not only common, but, in most cases, is probably very large.

(3) Are circular estimates useful measures of effect size?

Yes and no. They’re less useful than unbiased measures of effect size. But given that the vast majority of effects reported in whole-brain fMRI analyses (and, more generally, analyses in most fields) are likely to be inflated to some extent, the only way to ensure we don’t rely on circular estimates of effect size would be to disregard effect size estimates entirely, which doesn’t seem prudent.

(4) Should circular estimates of effect size be presented in papers and, if so, how?

Yes, because the only principled alternatives are to either (a) never report effect sizes (which seems much too drastic), or (b) report the results of every single test performed, irrespective of the result (i.e., to never give selection bias an opportunity to rear its head). Neither of these is reasonable. We should generally report effect sizes for all key effects, but they should be accompanied by appropriate confidence intervals. As Lindquist notes:

In general, it may be useful to present any effect size estimate as confidence intervals, so that readers can see for themselves how much uncertainty is related to the point estimate.

A key point I’d add is that the width of the reported CIs should match the threshold used to identify results in the first place. In other words, if you conduct a whole brain analysis at p < .001, you should report all resulting effects with 99.9% CIs, and not 95% CIs. I think this simple step would go a considerable ways towards conveying the true uncertainty surrounding most point estimates in fMRI studies.

(5) Are effect size estimates important/useful for neuroscience research, and why?

I think my view here is closest to Ed Vul’s:

Yes, very much so. Null-hypothesis testing is insufficient for most goals of neuroscience because it can only indicate that a brain region is involved to some nonzero degree in some task contrast. This is likely to be true of most combinations of task contrasts and brain regions when measured with sufficient power.

I’d go further than Ed does though, and say that in a sense, effect size estimates are the only things that matter. As Ed notes, there are few if any cases where it’s plausible to suppose that the effect of some manipulation on brain activation is really zero. The brain is a very dense causal system–almost any change in one variable is going to have downstream effects on many, and perhaps most, others. So the real question we care about is almost never “is there or isn’t there an effect,” it’s whether there’s an effect that’s big enough to actually care about. (This problem isn’t specific to fMRI research, of course; it’s been a persistent source of criticism of null hypothesis significance testing for many decades.)

People sometimes try to deflect this concern by saying that they’re not trying to make any claims about how big an effect is, but only about whether or not one can reject the null–i.e., whether any kind of effect is present or not. I’ve never found this argument convincing, because whether or not you own up to it, you’re always making an effect size claim whenever you conduct a hypothesis test. Testing against a null of zero is equivalent to saying that you care about any effect that isn’t exactly zero, which is simply false. No one in fMRI research cares about r or d values of 0.0001, yet we routinely conduct tests whose results could be consistent with those types of effect sizes.

Since we’re always making implicit claims about effect sizes when we conduct hypothesis tests, we may as well make them explicit so that they can be evaluated properly. If you only care about correlations greater than 0.1, there’s no sense in hiding that fact; why not explicitly test against a null range of -0.1 to 0.1, instead of a meaningless null of zero?

(6) What is the best way to accurately estimate effect sizes from imaging data?

Use large samples, conduct multivariate analyses, report results comprehensively, use meta-analysis… I don’t think there’s any single way to ensure accurate effect size estimates, but plenty of things help. Maybe the most general recommendation is to ensure adequate power (see below), which will naturally minimize effect size inflation.

(7) What makes data sets independent? Are different sets of subjects required?

Most of the authors think (as I do too) that different sets of subjects are indeed required in order to ensure independence. Here’s Nichols:

Only data sets collected on distinct individuals can be assured to be independent. Splitting an individual’s data (e.g., using run 1 and run 2 to create two data sets) does not yield independence at the group level, as each subject’s true random effect will correlate the data sets.

Put differently, splitting data within subjects only eliminates measurement error, and not sampling error. You could in theory measure activation perfectly reliably (in which case the two halves of subjects’ data would be perfectly correlated) and still have grossly inflated effects, simply because the multivariate distribution of scores in your sample doesn’t accurately reflect the distribution in the population. So, as Nichols points out, you always need new subjects if you want to be absolutely certain your analyses are independent. But since this generally isn’t feasible, I’d argue we should worry less about whether or not our data sets are completely independent, and more about reporting results in a way that makes the presence of any bias as clear as possible.

(8) What information can one glean from data selected for a certain effect?

I think this is kind of a moot question, since virtually all data are susceptible to some form of selection bias (scientists generally don’t write papers detailing all the analyses they conducted that didn’t pan out!). As I note above, I think it’s a bad idea to disregard effect sizes entirely; they’re actually what we should be focusing most of our attention on. Better to report confidence intervals that accurately reflect the selection procedure and make the uncertainty around the point estimate clear.

(9) Are visualizations of nonindependent data helpful to illustrate the claims of a paper?

Not in cases where there’s an extremely strong dependency between the selection criteria and the effect size estimate. In cases of weak to moderate dependency, visualization is fine so long as confidence bands are plotted alongside the best fit. Again, the key is to always be explicit about the limitations of the analysis and provide some indication of the uncertainty involved.

(10) Should data exploration be discouraged in favor of valid confirmatory analyses?

No. I agree with Poldrack’s sentiment here:

Our understanding of brain function remains incredibly crude, and limiting research to the current set of models and methods would virtually guarantee scientific failure. Exploration of new approaches is thus critical, but the findings must be confirmed using new samples and convergent methods.

(11) Is a confirmatory analysis safer than an exploratory analysis in terms of drawing neuroscientific conclusions?

In principle, sure, but in practice, it’s virtually impossible to determine which reported analyses really started out their lives as confirmatory analyses and which started life out as exploratory analyses and then mysteriously evolved into “a priori” predictions once the paper was written. I’m not saying there’s anything wrong with this–everyone reports results strategically to some extent–just that I don’t know that the distinction between confirmatory and exploratory analyses is all that meaningful in practice. Also, as the previous point makes clear, safety isn’t the only criterion we care about; we also want to discover new and unexpected findings, which requires exploration.

(12) What makes a whole-brain mapping analysis valid? What constitutes sufficient adjustment for multiple testing?

From a hypothesis testing standpoint, you need to ensure adequate control of the family-wise error (FWE) rate or false discovery rate (FDR). But as I suggested above, I think this only ensures validity in a limited sense; it doesn’t ensure that the results are actually going to be worth caring about. If you want to feel confident that any effects that survive are meaningfully large, you need to do the extra work up front and define what constitutes a meaningful effect size (and then test against that).

(13) How much power should a brain-mapping analysis have to be useful?

As much as possible! Concretely, the conventional target of 80% seems like a good place to start. But as I’ve argued before (e.g., here), that would require more than doubling conventional sample sizes in most cases. The reality is that fMRI studies are expensive, so we’re probably stuck with underpowered analyses for the foreseeable future. So we need to find other ways to compensate for that (e.g., relying more heavily on meta-analytic effect size estimates).

(14) In which circumstances are nonindependent selective analyses acceptable for scientific publication?

It depends on exactly what’s problematic about the analysis. Analyses that are truly circular and provide no new information should never be reported, but those constitute only a small fraction of all analyses. More commonly, the nonindependence simply amounts to selection bias: researchers tend to report only those results that achieve statistical significance, thereby inflating apparent effect sizes. I think the solution to this is to still report all key effect sizes, but to ensure they’re accompanied by confidence intervals and appropriate qualifiers.

Kriegeskorte N, Lindquist MA, Nichols TE, Poldrack RA, & Vul E (2010). Everything you never wanted to know about circular analysis, but were afraid to ask. Journal of cerebral blood flow and metabolism : official journal of the International Society of Cerebral Blood Flow and Metabolism PMID: 20571517

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.”

There’s a time-honored tradition in the social sciences–or at least psychology–that goes something like this. You decide on some provisional number of subjects you’d like to run in your study; usually it’s a nice round number like twenty or sixty, or some number that just happens to coincide with the sample size of the last successful study you ran. Or maybe it just happens to be your favorite number (which of course is forty-four). You get your graduate student to start running the study, and promptly forget about it for a couple of weeks while you go about writing up journal reviews that are three weeks overdue and chapters that are six months overdue.

A few weeks later, you decide you’d like to know how that Amazing New Experiment you’re running is going. You summon your RA and ask him, in magisterial tones, “how’s that Amazing New Experiment we’re running going?” To which he falteringly replies that he’s been very busy with all the other data entry and analysis chores you assigned him, so he’s only managed to collect data from eighteen subjects so far. But he promises to have the other eighty-two subjects done any day now.

“Not to worry,” you say. “We’ll just take a peek at the data now and see what it looks like; with any luck, you won’t even need to run any more subjects! By the way, here are my car keys; see if you can’t have it washed by 5 pm. Your job depends on it. Ha ha.”

Once your RA’s gone to soil himself somewhere, you gleefully plunge into the task of peeking at your data. You pivot your tables, plyr your data frame, and bravely sort your columns. Then you extract two of the more juicy variables for analysis, and after some careful surgery a t-test or six, you arrive at the conclusion that your hypothesis is… “marginally” supported. Which is to say, the magical p value is somewhere north of .05 and somewhere south of .10, and now it’s just parked by the curb waiting for you to give it better directions.

You briefly contemplate reporting your result as a one-tailed test–since it’s in the direction you predicted, right?–but ultimately decide against that. You recall the way your old Research Methods professor used to rail at length against the evils of one-sample tests, and even if you don’t remember exactly why they’re so evil, you’re not willing to take any chances. So you decide it can’t be helped; you need to collect some more data.

You summon your RA again. “Is my car washed yet?” you ask.

“No,” says your RA in a squeaky voice. “You just asked me to do that fifteen minutes ago.”

“Right, right,” you say. “I knew that.”

You then explain to your RA that he should suspend all other assigned duties for the next few days and prioritize running subjects in the Amazing New Experiment. “Abandon all other tasks!” you decree. “If it doesn’t involve collecting new data, it’s unimportant! Your job is to eat, sleep, and breathe new subjects! But not literally!”

Being quite clever, your RA sees an opening. “I guess you’ll want your car keys back, then,” he suggests.

“Nice try, Poindexter,” you say. “Abandon all other tasks… starting tomorrow.”

You also give your RA very careful instructions to email you the new data after every single subject, so that you can toss it into your spreadsheet and inspect the p value at every step. After all, there’s no sense in wasting perfectly good data; once your p value is below .05, you can just funnel the rest of the participants over to the Equally Amazing And Even Newer Experiment you’ve been planning to run as a follow-up. It’s a win-win proposition for everyone involved. Except maybe your RA, who’s still expected to return triumphant with a squeaky clean vehicle by 5 pm.

Twenty-six months and four rounds of review later, you publish the results of the Amazing New Experiment as Study 2 in a six-study paper in the Journal of Ambiguous Results. The reviewers raked you over the coals for everything from the suggested running head of the paper to the ratio between the abscissa and the ordinate in Figure 3. But what they couldn’t argue with was the p value in Study 2, which clocked in at just under p < .05, with only 21 subjects’ worth of data (compare that to the 80 you had to run in Study 4 to get a statistically significant result!). Suck on that, Reviewers!, you think to yourself pleasantly while driving yourself home from work in your shiny, shiny Honda Civic.

So ends our short parable, which has at least two subtle points to teach us. One is that it takes a really long time to publish anything; who has time to wait twenty-six months and go through four rounds of review?

The other, more important point, is that the desire to peek at one’s data, which often seems innocuous enough–and possibly even advisable (quality control is important, right?)–can actually be quite harmful. At least if you believe that the goal of doing research is to arrive at the truth, and not necessarily to publish statistically significant results.

The basic problem is that peeking at your data is rarely a passive process; most often, it’s done in the context of a decision-making process, where the goal is to determine whether or not you need to keep collecting data. There are two possible peeking outcomes that might lead you to decide to halt data collection: a very low p value (i.e., p < .05), in which case your hypothesis is supported and you may as well stop gathering evidence; or a very high p value, in which case you might decide that it’s unlikely you’re ever going to successfully reject the null, so you may as well throw in the towel. Either way, you’re making the decision to terminate the study based on the results you find in a provisional sample.

A complementary situation, which also happens not infrequently, occurs when you collect data from exactly as many participants as you decided ahead of time, only to find that your results aren’t quite what you’d like them to be (e.g., a marginally significant hypothesis test). In that case, it may be quite tempting to keep collecting data even though you’ve already hit your predetermined target. I can count on more than one hand the number of times I’ve overheard people say (often without any hint of guilt) something to the effect of “my p value’s at .06 right now, so I just need to collect data from a few more subjects.”

Here’s the problem with either (a) collecting more data in an effort to turn p < .06 into p < .05, or (b) ceasing data collection because you’ve already hit p < .05: any time you add another subject to your sample, there’s a fairly large probability the p value will go down purely by chance, even if there’s no effect. So there you are sitting at p < .06 with twenty-four subjects, and you decide to run a twenty-fifth subject. Well, let’s suppose that there actually isn’t a meaningful effect in the population, and that p < .06 value you’ve got is a (near) false positive. Adding that twenty-fifth subject can only do one of two things: it can raise your p value, or it can lower it. The exact probabilities of these two outcomes depends on the current effect size in your sample before adding the new subject; but generally speaking, they’ll rarely be very far from 50-50. So now you can see the problem: if you stop collecting data as soon as you get a significant result, you may well be capitalizing on chance. It could be that if you’d collected data from a twenty-sixth and twenty-seventh subject, the p value would reverse its trajectory and start rising. It could even be that if you’d collected data from two hundred subjects, the effect size would stabilize near zero. But you’d never know that if you stopped the study as soon as you got the results you were looking for.

Lest you think I’m exaggerating, and think that this problem falls into the famous class of things-statisticians-and-methodologists-get-all-anal-about-but-that-don’t-really-matter-in-the-real-world, here’s a sobering figure (taken from this chapter):

The figure shows the results of a simulation quantifying the increase in false positives associated with data peeking. The assumptions here are that (a) data peeking begins after about 10 subjects (starting earlier would further increase false positives, and starting later would decrease false positives somewhat), (b) the researcher stops as soon as a peek at the data reveals a result significant at p < .05, and (c) data peeking occurs at incremental steps of either 1 or 5 subjects. Given these assumptions, you can see that there’s a fairly monstrous rise in the actual Type I error rate (relative to the nominal rate of 5%). For instance, if the researcher initially plans to collect 60 subjects, but peeks at the data after every 5 subjects, there’s approximately a 17% chance that the threshold of p < .05 will be reached before the full sample of 60 subjects is collected. When data peeking occurs even more frequently (as might happen if a researcher is actively trying to turn p < .07 into p < .05, and is monitoring the results after each incremental participant), Type I error inflation is even worse. So unless you think there’s no practical difference between a 5% false positive rate and a 15 – 20% false positive rate, you should be concerned about data peeking; it’s not the kind of thing you just brush off as needless pedantry.

How do we stop ourselves from capitalizing on chance by looking at the data? Broadly speaking, there are two reasonable solutions. One is to just pick a number up front and stick with it. If you commit yourself to collecting data from exactly as many subjects as you said you would (you can proclaim the exact number loudly to anyone who’ll listen, if you find it helps), you’re then free to peek at the data all you want. After all, it’s not the act of observing the data that creates the problem; it’s the decision to terminate data collection based on your observation that matters.

The other alternative is to explicitly correct for data peeking. This is a common approach in large clinical trials, where data peeking is often ethically mandated, because you don’t want to either (a) harm people in the treatment group if the treatment turns out to have clear and dangerous side effects, or (b) prevent the control group from capitalizing on the treatment too if it seems very efficacious. In either event, you’d want to terminate the trial early. What researchers often do, then, is pick predetermined intervals at which to peek at the data, and then apply a correction to the p values that takes into account the number of, and interval between, peeking occasions. Provided you do things systematically in that way, peeking then becomes perfectly legitimate. Of course, the downside is that having to account for those extra inspections of the data makes your statistical tests more conservative. So if there aren’t any ethical issues that necessitate peeking, and you’re not worried about quality control issues that might be revealed by eyeballing the data, your best bet is usually to just pick a reasonable sample size (ideally, one based on power calculations) and stick with it.

Oh, and also, don’t make your RAs wash your car for you; that’s not their job.

Cosma Shalizi has a post up today discussing a new paper he wrote with Andrew C. Thomas arguing that it’s pretty much impossible to distinguish the effects of social contagion from homophily in observational studies.

That’s probably pretty cryptic without context, so here’s the background. A number of high-profile studies have been published in the past few years suggesting that everything from obesity to loneliness to pot smoking is socially contagious. The basic argument is that when you look at the diffusion of certain traits within social networks, you find that having friends who are obese is more likely to make you obese, having happy friends is more likely to make you happy, and so on. These effects (it’s been argued) persist even after you control for homophily–that is, the tendency of people to know and like other people who are similar to them–and can be indirect, so that you’re more likely to be obese even if your friends’ friends (who you may not even know know) are obese.

Needless to say, the work has been controversial. A few weeks ago, Dave Johns wrote an excellent pair of articles in Slate describing the original research, as well as the recent critical backlash (see also Andrew Gelman’s post here). Much of the criticism has focused on the question of whether it’s really possible to distinguish homophily from contagion using the kind of observational data and methods that contagion researchers have relied on. That is, if the probability that you’ll become obese (or lonely, or selfish, etc.) increases as a function of the number of obese people you know, is that because your acquaintance with obese people exerts a causal influence on your own body weight (e.g., by shaping your perception of body norms, eating habits, etc.), or is it simply that people with a disposition to become obese tend to seek out other people with the same disposition, and there’s no direct causal influence at all? It’s an important question, but one that’s difficult to answer conclusively.

In their new paper, Shalizi and Thomas use an elegant combination of logical argumentation, graphical causal models, and simulation to show that, in general, contagion effects are unidentifiable: you simply can’t tell whether like begets like because of a direct causal influence (“real” contagion), or because of homophily (birds of a feather flocking together). The only way out of the bind is to make unreasonably strong assumptions–e.g., that the covariates explicitly included in one’s model capture all of the influence of latent traits on observable behaviors. In his post Shalizi sums up the conclusions of the paper this way:

What the statistician or social scientist sees is that bridge-jumping is correlated across the social network. In this it resembles many, many, many behaviors and conditions, such as prescribing new antibiotics (one of the classic examples), adopting other new products, adopting political ideologies, attaching tags to pictures on flickr, attaching mis-spelled jokes to pictures of cats, smoking, drinking, using other drugs, suicide, literary tastes, coming down with infectious diseases, becoming obese, and having bad acne or being tall for your age. For almost all of these conditions or behaviors, our data is purely observational, meaning we cannot, for one reason or another, just push Joey off the bridge and see how Irene reacts. Can we nonetheless tell whether bridge-jumping spreads by (some form) of contagion, or rather is due to homophily, or, if it is both, say how much each mechanism contributes?

A lot of people have thought so, and have tried to come at it in the usual way, by doing regression. Most readers can probably guess what I think about that, so I will just say: don’t you wish. More sophisticated ideas, like propensity score matching, have also been tried, but people have pretty much assumed that it was possible to do this sort of decomposition. What Andrew and I showed is that in fact it isn’t, unless you are willing to make very strong, and generally untestable, assumptions.

It’s a very clear and compelling paper, and definitely worth reading if you have any interest at all in the question of whether and when it’s okay to apply causal modeling techniques to observational data. The answer Shalizi’s argued for on many occasions–and an unfortunate one from many scientists’ perspective–seems to be: very rarely if ever.

In the last year or so, I’ve been experimenting with different ways of displaying correlation matrices, and have gotten very fond of color-coded correlograms. Here’s one from a paper I wrote investigating the relationship between personality and word use among bloggers (click to enlarge):

The rows reflect language categories from Jamie Pennebaker’s Linguistic Inquiry and Word Count (LIWC) dictionary; the columns reflect Extraversion scores (first column) or scores on the lower-order “facets” of Extraversion (as measured by the IPIP version of the NEO-PI-R). The plot was generated in R using code adapted from the corrgram package (R really does have contributed packages for everything). Positive correlations are in blue, negative ones are in red.

The thing I really like about these figures is that the colors instantly orient you to the most important features of the correlation matrix, instead of having to inspect every cell for the all-important ***magical***asterisks***of***statistical***significance***. For instance, a cursory glance tells you that even though Excitement-Seeking and Cheerfulness are both nominally facets of Extraversion, they’re associated with very different patterns of word use. And then a slightly less cursory glance tells you that that’s because people with high Excitement-Seeking scores like to swear a lot and use negative emotion words, while Cheerful people like to talk about friends, music, and use positive emotional language. You’d get the same information without the color, of course, but it’d take much longer to extract,  and then you’d have to struggle to keep all of the relevant numbers in mind while you mull them over. The colors do a lot to reduce cognitive load, and also have the secondary benefit of looking pretty.

If you’re interested in using correlograms, a good place to start is the Quick-R tutorial on correlograms in R. The documentation for the corrgram package is here, and there’s a nice discussion of the principles behind the visual display of correlation matrices in this article.

p.s. I’m aware this post has the worst title ever; the sign-up sheet for copy editing duties is in the comment box (hint hint).

There’s a feature article in the new issue of Science News on the failure of science “to face the shortcomings of statistics”. The author, Tom Siegfried, argues that many scientific results shouldn’t be believed because they depend on faulty statistical practices:

Even when performed correctly, statistical tests are widely misunderstood and frequently misinterpreted. As a result, countless conclusions in the scientific literature are erroneous, and tests of medical dangers or treatments are often contradictory and confusing.

I have mixed feelings about the article. It’s hard to disagree with the basic idea that many scientific results are the results of statistical malpractice and/or misfortune. And Siegfried generally provides lucid explanations of some common statistical pitfalls when he sticks to the descriptive side of things. For instance, he gives nice accounts of Bayesian inference, of the multiple comparisons problem, and of the distinction between statistical significance and clinical/practical significance. And he nicely articulates what’s wrong with one of the most common (mis)interpretations of p values:

Correctly phrased, experimental data yielding a P value of .05 means that there is only a 5 percent chance of obtaining the observed (or more extreme) result if no real effect exists (that is, if the no-difference hypothesis is correct). But many explanations mangle the subtleties in that definition. A recent popular book on issues involving science, for example, states a commonly held misperception about the meaning of statistical significance at the .05 level: “This means that it is 95 percent certain that the observed difference between groups, or sets of samples, is real and could not have arisen by chance.”

So as a laundry list of common statistical pitfalls, it works quite nicely.

What I don’t really like about the article is that it seems to lay the blame squarely on the use of statistics to do science, rather than the way statistical analysis tends to be performed. That’s to say, a lay person reading the article could well come away with the impression that the very problem with science is that it relies on statistics. As opposed to the much more reasonable conclusion that science is hard, and statistics is hard, and ensuring that your work sits at the intersection of good science and good statistical practice is even harder. Siegfried all but implies that scientists are silly to base their conclusions on statistical inference. For instance:

It’s science’s dirtiest secret: The “scientific method” of testing hypotheses by statistical analysis stands on a flimsy foundation. Statistical tests are supposed to guide scientists in judging whether an experimental result reflects some real effect or is merely a random fluke, but the standard methods mix mutually inconsistent philosophies and offer no meaningful basis for making such decisions.

Or:

Experts in the math of probability and statistics are well aware of these problems and have for decades expressed concern about them in major journals. Over the years, hundreds of published papers have warned that science’s love affair with statistics has spawned countless illegitimate findings. In fact, if you believe what you read in the scientific literature, you shouldn’t believe what you read in the scientific literature.

The problem is that there isn’t really any viable alternative to the “love affair with statistics”. Presumably Siegfried doesn’t think (most) scientists ought to be doing qualitative research; so the choice isn’t between statistics and no statistics, it’s between good and bad statistics.

In that sense, the tone of a lot of the article is pretty condescending: it comes off more like Siegfried saying “boy, scientists sure are dumb” and less like the more accurate observation that doing statistics is really hard, and it’s not surprising that even very smart people mess up frequently.

What makes it worse is that Siegfried slips up on a couple of basic points himself, and says some demonstrably false things in a couple of places. For instance, he explains failures to replicate genetic findings this way:

Nowhere are the problems with statistics more blatant than in studies of genetic influences on disease. In 2007, for instance, researchers combing the medical literature found numerous studies linking a total of 85 genetic variants in 70 different genes to acute coronary syndrome, a cluster of heart problems. When the researchers compared genetic tests of 811 patients that had the syndrome with a group of 650 (matched for sex and age) that didn’t, only one of the suspect gene variants turned up substantially more often in those with the syndrome — a number to be expected by chance.

“Our null results provide no support for the hypothesis that any of the 85 genetic variants tested is a susceptibility factor” for the syndrome, the researchers reported in the Journal of the American Medical Association.

How could so many studies be wrong? Because their conclusions relied on “statistical significance,” a concept at the heart of the mathematical analysis of modern scientific experiments.

This is wrong for at least two reasons. One is that, to believe the JAMA study Siegfried is referring to, and disbelieve the results of all 85 previously reported findings, you have to accept the null hypothesis, which is one of the very same errors Siegfried is supposed to be warning us against. In fact, you have to accept the null hypothesis 85 times. In the JAMA paper, the authors are careful to note that it’s possible the actual effects were simply overstated in the original studies, and that at least some of the original findings might still hold under more restrictive conditions. The conclusion that there really is no effect whatsoever is almost never warranted, because you rarely have enough power to rule out even very small effects. But Siegfried offers no such qualifiers; instead, he happily accepts 85 null hypotheses in support of his own argument.

The other issue is that it isn’t really the reliance on statistical significance that causes replication failures; it’s usually the use of excessively liberal statistical criteria. The problem has very little to do with the hypothesis testing framework per se. To see this, consider that if researchers always used a criterion of p < .0000001 instead of the conventional p < .05, there would almost never be any replication failures (because there would almost never be any statistically significant findings, period). So the problem is not so much with the classical hypothesis testing framework as with the choices many researchers make about how to set thresholds within that framework. (That’s not to say that there aren’t any problems associated with frequentist statistics, just that this isn’t really a fair one.)

Anyway, Siegfried’s explanations of the pitfalls of statistical significance then leads him to make what has to be hands-down the silliest statement in the article:

But in fact, there’s no logical basis for using a P value from a single study to draw any conclusion. If the chance of a fluke is less than 5 percent, two possible conclusions remain: There is a real effect, or the result is an improbable fluke. Fisher’s method offers no way to know which is which. On the other hand, if a study finds no statistically significant effect, that doesn’t prove anything, either. Perhaps the effect doesn’t exist, or maybe the statistical test wasn’t powerful enough to detect a small but real effect.

If you take this statement at face value, you should conclude there’s no point in doing statistical analysis, period. No matter what statistical procedure you use, you’re never going to know for cross-your-heart-hope-to-die sure that your conclusions are warranted. After all, you’re always going to have the same two possibilities: either the effect is real, or it’s not (or, if you prefer to frame the problem in terms of magnitude, either the effect is about as big as you think it is, or it’s very different in size). The same exact conclusion goes through if you take a threshold of p < .001 instead of one of p < .05: the effect can still be a spurious and improbable fluke. And it also goes through if you have twelve replications instead of just one positive finding: you could still be wrong (and people have been wrong). So saying that “two possible conclusions remain” isn’t offering any deep insight; it’s utterly vacuous.

The reason scientists use a conventional threshold of p < .05 when evaluating results isn’t because we think it gives us some magical certainty into whether a finding is “real” or not; it’s because it feels like a reasonable level of confidence to shoot for when making claims about whether the null hypothesis of no effect is likely to hold or not. Now there certainly are many problems associated with the hypothesis testing framework–some of them very serious–but if you really believe that “there’s no logical basis for using a P value from a single study to draw any conclusion,” your beef isn’t actually with p values, it’s with the very underpinnings of the scientific enterprise.

Anyway, the bottom line is Siegfried’s article is not so much bad as irresponsible. As an accessible description of some serious problems with common statistical practices, it’s actually quite good. But I guess the sense I got in reading the article was that at some point Siegfried became more interested in writing a contrarian piece about how scientists are falling down on the job than about how doing statistics well is just really hard for almost all of us (I certainly fail at it all the time!). And ironically, in the process of trying to explain just why “science fails to face the shortcomings of statistics”, Siegfried commits some of the very same errors he’s taking scientists to task for.

[UPDATE: Steve Novella says much the same thing here.]

[UPDATE 2: Andrew Gelman has a nice roundup of other comments on Siegfried's article throughout the blogosphere.]

This post shamelessly plagiarizes liberally borrows ideas from a much longer, more detailed, and just generally better post by Cosma Shalizi. I’m not apologetic, since I’m a firm believer in the notion that good ideas should be repeated often and loudly. So I’m going to be often and loud here, though I’ll try to be (slightly) more succinct than Shalizi. Still, if you have the time to spare, you should read his longer and more mathematical take.

There’s a widely held view among intelligence researchers in particular, and psychologists more generally, that there’s a general factor of intelligence (often dubbed g) that accounts for a very large portion of the variance in a broad range of cognitive performance tasks. Which is to say, if you have a bunch of people do a bunch of different tasks, all of which we think tap different aspects of intellectual ability, and then you take all those scores and factor analyze them, you’ll almost invariably get a first factor that explains 50% or more of the variance in the zero-order scores. Or to put it differently, if you know a person’s relative standing on g, you can make a reasonable prediction about how that person will do on lots of different tasks–for example, digit symbol substitution, N-back, go/no-go, and so on and so forth. Virtually all tasks that we think reflect cognitive ability turn out, to varying extents, to reflect some underlying latent variable, and that latent variable is what we dub g.

In a trivial sense, no one really disputes that there’s such a thing as g. You can’t really dispute the existence of g, seeing as a general factor tends to fall out of virtually all factor analyses of cognitive tasks; it’s about as well-replicated a finding as you can get. To say that g exists, on the most basic reading, is simply to slap a name on the empirical fact that scores on different cognitive measures tend to intercorrelate positively to a considerable extent.

What’s not so clear is what the implications of g are for our understanding of how the human mind and brain works. If you take the presence of g at face value, all it really says is what we all pretty much already know: some people are smarter than others. People who do well in one intellectual domain will tend to do pretty well in others too, other things being equal. With the exception of some people who’ve tried to argue that there’s no such thing as general intelligence, but only “multiple intelligences” that totally fractionate across domains (not a compelling story, if you look at the evidence), it’s pretty clear that cognitive abilities tend to hang together pretty well.

The trouble really crops up when we try to say something interesting about the architecture of the human mind on the basis of the psychometric evidence for g. If someone tells you that there’s a single psychometric factor that explains at least 50% of the variance in a broad range of human cognitive abilities, it seems perfectly reasonable to suppose that that’s because there’s some unitary intelligence system in people’s heads, and that that system varies in capacity across individuals. In other words, the two intuitive models people have about intelligence seem to be that either (a) there’s some general cognitive system that corresponds to g, and supports a very large portion of the complex reasoning ability we call “intelligence” or (b) there are lots of different (and mostly unrelated) cognitive abilities, each of which contributes only to specific types of tasks and not others. Framed this way, it just seems obvious that the former view is the right one, and that the latter view has been discredited by the evidence.

The problem is that the psychometric evidence for g stems almost entirely from statistical procedures that aren’t really supposed to be use for causal inference. The primary weapon in the intelligence researcher’s toolbox has historically been principal components analysis (PCA) or exploratory factor analysis, which are really just data reduction techniques. PCA tells you how you can describe your data in a more compact way, but it doesn’t actually tell you what structure is in your data. A good analogy is the use of digital compression algorithms. If you take a directory full of .txt files and compress them into a single .zip file, you’ll almost certainly end up with a file that’s only a small fraction of the total size of the original texts. The reason this works is because certain patterns tend to repeat themselves over and over in .txt files, and a smart algorithm will store an abbreviated description of those patterns rather than the patterns themselves. Which, conceptually, is almost exactly what happens when you run a PCA on a dataset: you’re searching for consistent patterns in the way observations vary along multiple variables, and discarding any redundancy you come across in favor of a more compact description.

Now, in a very real sense, compression is impressive. It’s certainly nice to be able to email your friend a 140kb .zip of your 1200-page novel rather than a 2mb .doc. But note that you don’t actually learn much from the compression. It’s not like your friend can open up that 140k binary representation of your novel, read it, and spare herself the torture of the other 1860kb. If you want to understand what’s going on in a novel, you need to read the novel and think about the novel. And if you want to understand what’s going on in a set of correlations between different cognitive tasks, you need to carefully inspect those correlations and carefully think about those correlations. You can run a factor analysis if you like, and you might learn something, but you’re not going to get any deep insights into the “true” structure of the data. The “true” structure of the data is, by definition, what you started out with (give or take some error). When you run a PCA, you actually get a distorted (but simpler!) picture of the data.

To most people who use PCA, or other data reduction techniques, this isn’t a novel insight by any means. Most everyone who uses PCA knows that in an obvious sense you’re distorting the structure of the data when you reduce its dimensionality. But the use of data reduction is often defended by noting that there must be some reason why variables hang together in such a way that they can be reduced to a much smaller set of variables with relatively little loss of variance. In the context of intelligence, the intuition can be expressed as: if there wasn’t really a single factor underlying intelligence, why would we get such a strong first factor? After all, it didn’t have to turn out that way; we could have gotten lots of smaller factors that appear to reflect distinct types of ability, like verbal intelligence, spatial intelligence, perceptual speed, and so on. But it did turn out that way, so that tells us something important about the unitary nature of intelligence.

This is a strangely compelling argument, but it turns out to be only minimally true. What the presence of a strong first factor does tell you is that you have a lot of positively correlated variables in your data set. To be fair, that is informative. But it’s only minimally informative, because, assuming you eyeballed the correlation matrix in the original data, you already knew that.

What you don’t know, and can’t know, on the basis of a PCA, is what underlying causal structure actually generated the observed positive correlations between your variables. It’s certainly possible that there’s really only one central intelligence system that contributes the bulk of the variance to lots of different cognitive tasks. That’s the g model, and it’s entirely consistent with the empirical data. Unfortunately, it’s not the only one. To the contrary, there are an infinite number of possible causal models that would be consistent with any given factor structure derived from a PCA, including a structure dominated by a strong first factor. In fact, you can have a causal structure with as many variables as you like be consistent with g-like data. So long as the variables in your model all make contributions in the same direction to the observed variables, you will tend to end up with an excessively strong first factor. So you could in principle have 3,000 distinct systems in the human brain, all completely independent of one another, and all of which contribute relatively modestly to a bunch of different cognitive tasks. And you could still get a first factor that accounts for 50% or more of the variance. No g required.

If you doubt this is true, go read Cosma Shalizi’s post, where he not only walks you through a more detailed explanation of the mathematical necessity of this claim, but also illustrates the point using some very simple simulations. Basically, he builds a toy model in which 11 different tasks each draw on several hundred underlying cognitive tasks, which are turn drawn from a larger pool of 2,766 completely independent abilities. He then runs a PCA on the data and finds, lo and behold, a single factor that explains nearly 50% of the variance in scores. Using PCA, it turns out, you can get something huge from (almost) nothing.

Now, at this point a proponent of a unitary g might say, sure, it’s possible that there isn’t really a single cognitive system underlying variation in intelligence; but it’s not plausible, because it’s surely more parsimonious to posit a model with just one variable than a model with 2,766. But that’s only true if you think that our brains evolved in order to make life easier for psychometricians, which, last I checked, wasn’t the case. If you think even a little bit about what we know about the biological and genetic bases of human cognition, it starts to seem really unlikely that there really could be a single central intelligence system. For starters, the evidence just doesn’t support it. In the cognitive neuroscience literature, for example, biomarkers of intelligence abound, and they just don’t seem all that related. There’s a really nice paper in Nature Reviews Neuroscience this month by Deary, Penke, and Johnson that reviews a substantial portion of the literature of intelligence; the upshot is that intelligence has lots of different correlates. For example, people who score highly on intelligence tend to (a) have larger brains overall; (b) show regional differences in brain volume; (c) show differences in neural efficiency when performing cognitive tasks; (d) have greater white matter integrity; (e) have brains with more efficient network structures;  and so on.

These phenomena may not all be completely independent, but it’s hard to believe there’s any plausible story you could tell that renders them all part of some unitary intelligence system, or subject to unitary genetic influence. And really, why should they be part of a unitary system? Is there really any reason to think there has to be a single rate-limiting factor on performance? It’s surely perfectly plausible (I’d argue, much more plausible) to think that almost any complex cognitive task you use as an index of intelligence is going to draw on many, many different cognitive abilities. Take a trivial example: individual differences in visual acuity probably make a (very) small contribution to performance on many different cognitive tasks. If you can’t see the minute details of the stimuli as well as the next person, you might perform slightly worse on the task. So some variance in putatively “cognitive” task performance undoubtedly reflects abilities that most intelligence researchers wouldn’t really consider properly reflective of higher cognition at all. And yet, that variance has to go somewhere when you run a factor analysis. Most likely, it’ll go straight into that first factor, or g, since it’s variance that’s common to multiple tasks (i.e., someone with poorer eyesight may tend to do very slightly worse on any task that requires visual attention). In fact, any ability that makes unidirectional contributions to task performance, no matter how relevant or irrelevant to the conceptual definition of intelligence, will inflate the so-called g factor.

If this still seems counter-intuitive to you, here’s an analogy that might, to borrow Dan Dennett’s phrase, prime your intuition pump (it isn’t as dirty as it sounds). Imagine that instead of studying the relationship between different cognitive tasks, we decided to study the relation between performance at different sports. So we went out and rounded up 500 healthy young adults and had them engage in 16 different sports, including basketball, soccer, hockey, long-distance running, short-distance running, swimming, and so on. We then took performance scores for all 16 tasks and submitted them to a PCA. What do you think would happen? I’d be willing to bet good money that you’d get a strong first factor, just like with cognitive tasks. In other words, just like with g, you’d have one latent variable that seemed to explain the bulk of the variance in lots of different sports-related abilities. And just like g, it would have an easy and parsimonious interpretation: a general factor of athleticism!

Of course, in a trivial sense, you’d be right to call it that. I doubt anyone’s going to deny that some people just are more athletic than others. But if you then ask, “well, what’s the mechanism that underlies athleticism,” it’s suddenly much less plausible to think that there’s a single physiological variable or pathway that supports athleticism. In fact, it seems flatly absurd. You can easily think of dozens if not hundreds of factors that should contribute a small amount of the variance to performance on multiple sports. To name just a few: height, jumping ability, running speed, oxygen capacity, fine motor control, gross motor control, perceptual speed, response time, balance, and so on and so forth. And most of these are individually still relatively high-level abilities that break down further at the physiological level (e.g., “balance” is itself a complex trait that at minimum reflects contributions of the vestibular, visual, and cerebellar systems, and so on.). If you go down that road, it very quickly becomes obvious that you’re just not going to find a unitary mechanism that explains athletic ability. Because it doesn’t exist.

All of this isn’t to say that intelligence (or athleticism) isn’t “real”. Intelligence and athleticism are perfectly real; it makes complete sense, and is factually defensible, to talk about some people being smarter or more athletic than other people. But the point is that those judgments are based on superficial observations of behavior; knowing that people’s intelligence or athleticism may express itself in a (relatively) unitary fashion doesn’t tell you anything at all about the underlying causal mechanisms–how many of them there are, or how they interact.

As Cosma Shalizi notes, it also doesn’t tell you anything about heritability or malleability. The fact that we tend to think intelligence is highly heritable doesn’t provide any evidence in favor of a unitary underlying mechanism; it’s just as plausible to think that there are many, many individual abilities that contribute to complex cognitive behavior, all of which are also highly heritable individually. Similarly, there’s no reason to think our cognitive abilities would be any less or any more malleable depending on whether they reflect the operation of a single system or hundreds of variables. Regular physical exercise clearly improves people’s capacity to carry out all sorts of different activities, but that doesn’t mean you’re only training up a single physiological pathway when you exercise; a whole host of changes are taking place throughout your body.

So, assuming you buy the basic argument, where does that leave us? Depends. From a day-to-day standpoint, nothing changes. You can go on telling your friends that so-and-so is a terrific athlete but not the brightest crayon in the box, and your friends will go on understanding exactly what you meant. No one’s suggesting that intelligence isn’t stable and trait-like, just that, at the biological level, it isn’t really one stable trait.

The real impact of relaxing the view that g is a meaningful construct at the biological level, I think, will be in removing an artificial and overly restrictive constraint on researchers’ theorizing. The sense I get, having done some work on executive control, is that g is the 800-pound gorilla in the room: researchers interested in studying the neural bases of intelligence (or related constructs like executive or cognitive control) are always worrying about how their findings relate to g, and how to explain the fact that there might be dissociable neural correlates of different abilities (or even multiple independent contributions to fluid intelligence). To show you that I’m not making this concern up, and that it weighs heavily on many researchers, here’s a quote from the aforementioned and otherwise really excellent NRN paper by Deary et al reviewing recent findings on the neural bases of intelligence:

The neuroscience of intelligence is constrained by — and must explain — the following established facts about cognitive test performance: about half of the variance across varied cognitive tests is contained in general cognitive ability; much less variance is contained within broad domains of capability; there is some variance in specific abilities; and there are distinct ageing patterns for so-called fluid and crystallized aspects of cognitive ability.

The existence of g creates a complicated situation for neuroscience. The fact that g contributes substantial variance to all specific cognitive ability tests is generally thought to indicate that g contributes directly in some way to performance on those tests. That is, when domains of thinking skill (such as executive function and memory) or specific tasks (such as mental arithmetic and non-verbal reasoning on the Raven’s Progressive Matrices test) are studied, neuroscientists are observing brain activity related to g as well as the specific task activities. This undermines the ability to determine localized brain activities that are specific to the task at hand.

I hope I’ve convinced you by this point that the neuroscience of intelligence doesn’t have to explain why half of the variance is contained in general cognitive ability, because there’s no good evidence that there is such a thing as general cognitive ability (except in the descriptive psychometric sense, which carries no biological weight). Relaxing this artificial constraint would allow researchers to get on with the interesting and important business of identifying correlates (and potential causal determinants) of different cognitive abilities without having to worry about the relation of their finding to some Grand Theory of Intelligence. If you believe in g, you’re going to be at a complete loss to explain how researchers can continually identify new biological and genetic correlates of intelligence, and how the effect sizes could be so small (particularly at a genetic level, where no one’s identified a single polymorphism that accounts for more than a fraction of the observable variance in intelligence–the so called problem of “missing heritability”). But once you discard the fiction of g, you can take such findings in stride, and can set about the business of building integrative models that allow for and explicitly model the presence of multiple independent contributions to intelligence. And if studying the brain has taught us anything at all, it’s that the truth is inevitably more complicated than what we’d like to believe.

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.

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

Continuing along on their guided tour of Data I Wish I Had Access To, the OKCupid folks have posted another set of interesting figures on their blog. This time, they make the case for dating older women, suggesting that men might get more bang for their buck (in a literal sense, I suppose) by trying to contact women their age or older, rather than trying to hit on the young ‘uns. Men, it turns out, are creepy. Here’s how creepy:

Actually, that’s not so creepy. All it says is that men say they prefer to date younger women. That’s not going to shock anyone. This one is creepier:

The reason it’s creepy is that it basically says that, irrespective of what age ranges men say they find acceptable in a potential match, they’re actually all indiscriminately messaging 18-year old women. So basically, if you’re a woman on OKCupid who’s searching for that one special, non-creepy guy, be warned: they don’t exist. They’re pretty much all going to be eying 18-year olds for the rest of their lives. (To be fair, women also show a tendency to contact men below their lowest reported acceptable age. But it’s a much weaker effect; 40-year old women only occasionally try to hit on 24-year old guys, and tend to stay the hell away from the not-yet-of-drinking-age male population.)

Anyway, using this type of data, the OKCupid folks then generate this figure:

…which also will probably surprise no one, as it basically says women are most desirable when they’re young, and men when they’re (somewhat) older. But what the OKCupid folks then suggest is that it would be to men’s great advantage to broaden their horizons, because older women (which, in their range-restricted population, basically means anything over 30) self-report being much more interested in having sex more often, having casual sex, and using protection. I won’t bother hotlinking to all of those images, but here’s where they’re ultimately going with this:

I’m not going to comment on the appropriateness of trying to nudge one’s male userbase in the direction of more readily available casual sex (though I suspect they don’t need much nudging anyway). What I do wonder is to what extent these results reflect selection effects rather than a genuine age difference. The OKCupid folks suggest that women’s sexual interest increases as they age, which seems plausible given the conventional wisdom that women peak sexually in their 30s. But the effects in this case look pretty huge (unless the color scheme is misleading, which it might be; you’ll have to check out the post for the neat interactive flash animations), and it seems pretty plausible that much of the age effect could be driven by selection bias. Women with a more monogamous orientation are probably much more likely to be in committed, stable relationships by the time they turn 30 or 35, and probably aren’t scanning OKCupid for potential mates. Women who are in their 30s and 40s and still using online dating services are probably those who weren’t as interested in monogamous relationships to begin with. (Of course, the same is probably true of older men. Except that since men of all ages appear to be pretty interested in casual sex, there’s unlikely to be an obvious age differential.)

The other thing I’m not clear on is whether these analyses control for the fact that the userbase is heavily skewed toward younger users:

The people behind OKCupid are all mathematicians by training, so I’d be surprised if they hadn’t taken the underlying age distribution into consideration. But they don’t say anything about it in their post. The worry is that, if the base rate of different age groups isn’t taken into consideration, the heat map displayed above could be quite misleading. Given that there are many, many more 25-year old women on OKCupid than 35-year old women, failing to normalize properly would almost invariably make it look like there’s a heavy skew for men to message relatively younger women, irrespective of the male sender’s age. By the same token, it’s not clear that it’d be good advice to tell men to seek out older women, given that there are many fewer older women in the pool to begin with. As a thought experiment, suppose that the entire OKCupid male population suddenly started messaging women 5 years older than them, and entirely ignored their usual younger targets. The hit rate wouldn’t go up; it would probably actually fall precipitously, since there wouldn’t be enough older women to keep all the younger men entertained (at least, I certainly hope there wouldn’t). No doubt there’s a stable equilibrium point somewhere, where men and women are each targeting exactly the right age range to maximize their respective chances. I’m just not sure that it’s in OKCupid’s proposed “zone of greatness” for the men.

It’s also a bit surprising that OKCupid didn’t break down the response rate to people of the opposite gender as a function of the sender and receiver’s age. They’ve done this in the past, and it seems like the most direct way of testing whether men are more likely to get lucky by messaging older or younger women. Without knowing whether older women are actually responding to younger men’s overtures, it’s kind of hard to say what it all means. Except that I’d still kill to have their data.

What follows is a fictional piece about sheep and statistics. I wrote it about two years ago, intending it to serve as a preface to an article on the dangers of inadvertent data fudging. But then I decided that no journal editor in his or her right mind would accept an article that started out talking about thinking sheep. And anyway, the rest of the article wasn’t very good. So instead, I post this parable here for your ovine amusement. There’s a moral to the story, but I’m too lazy to write about it at the moment.

A shepherd named Zoltan lived in a small village in the foothills of the Carpathian Mountains. He tended to a flock of twelve sheep: Soffia, Krystyna, Anastasia, Orsolya, Marianna, Zigana, Julinka, Rozalia, Zsa Zsa, Franciska, Erzsebet, and Agi. Zoltan was a keen observer of animal nature, and would often point out the idiosyncracies of his sheep’s behavior to other shepherds whenever they got together.

“Anastasia and Orsolya are BFFs. Whatever one does, the other one does too. If Anastasia starts licking her face, Orsolya will too; if Orsolya starts bleating, Anastasia will start harmonizing along with her.”

“Julinka has a limp in her left leg that makes her ornery. She doesn’t want your pity, only your delicious clovers.”

“Agi is stubborn but logical. You know that old saying, spare the rod and spoil the sheep? Well, it doesn’t work for Agi. You need calculus and rhetoric with Agi.”

Zoltan’s colleagues were so impressed by these insights that they began to encourage him to record his observations for posterity.

“Just think, Zoltan,” young Gergely once confided. “If something bad happened to you, the world would lose all of your knowledge. You should write a book about sheep and give it to the rest of us. I hear you only need to know six or seven related things to publish a book.”

On such occasions, Zoltan would hem and haw solemnly, mumbling that he didn’t know enough to write a book, and that anyway, nothing he said was really very important. It was false modestly of course; in reality, he was deeply flattered, and very much concerned that his vast body of sheep knowledge would disappear along with him one day. So one day, Zoltan packed up his knapsack, asked Gergely to look after his sheep for the day, and went off to consult with the wise old woman who lived in the next village.

The old woman listened to Zoltan’s story with a good deal of interest, nodding sagely at all the right moments. When Zoltan was done, the old woman mulled her thoughts over for a while.

“If you want to be taken seriously, you must publish your findings in a peer-reviewed journal,” she said finally.

“What’s Pier Evew?” asked Zoltan.

“One moment,” said the old woman, disappearing into her bedroom. She returned clutching a dusty magazine. “Here,” she said, handing the magazine to Zoltan. “This is peer review.”

That night, after his sheep had gone to bed, Zoltan stayed up late poring over Vol. IV, Issue 5 of Domesticated Animal Behavior Quarterly. Since he couldn’t understand the figures in the magazine, he read it purely for the articles. By the time he put the magazine down and leaned over to turn off the light, the first glimmerings of an empirical research program had begun to dance around in his head. Just like fireflies, he thought. No, wait, those really were fireflies. He swatted them away.

“I like this… science,” he mumbled to himself as he fell asleep.

In the morning, Zoltan went down to the local library to find a book or two about science. He checked out a volume entitled Principia Scientifica Buccolica—a masterful derivation from first principles of all of the most common research methods, with special applications to animal behavior. By lunchtime, Zoltan had covered t-tests, and by bedtime, he had mastered Mordenkainen’s correction for inestimable herds.

In the morning, Zoltan made his first real scientific decision.

“Today I’ll collect some pilot data,” he thought to himself, “and tomorrow I’ll apply for an R01.”

His first set of studies tested the provocative hypothesis that sheep communicate with one another by moving their ears back and forth in Morse code. Study 1 tested the idea observationally. Zoltan and two other raters (his younger cousins), both blind to the hypothesis, studied sheep in pairs, coding one sheep’s ear movements and the other sheep’s behavioral responses. Studies 2 through 4 manipulated the sheep’s behavior experimentally. In Study 2, Zoltan taped the sheep’s ears to their head; in Study 3, he covered their eyes with opaque goggles so that they couldn’t see each other’s ears moving. In Study 4, he split the twelve sheep into three groups of four in order to determine whether smaller groups might promote increased sociability.

That night, Zoltan minded the data. “It’s a lot like minding sheep,” Zoltan explained to his cousin Griga the next day. “You need to always be vigilant, so that a significant result doesn’t get away from you.”

Zoltan had been vigilant, and the first 4 studies produced a number of significant results. In Study 1, Zoltan found that sheep appeared to coordinate ear twitches: if one sheep twitched an ear several times in a row, it was a safe bet that other sheep would start to do the same shortly thereafter (p < .01). There was, however, no coordination of licking, headbutting, stamping, or bleating behaviors, no matter how you sliced and diced it. “It’s a highly selective effect,” Zoltan concluded happily. After all, when you thought about it, it made sense. If you were going to pick just one channel for sheep to communicate through, ear twitching was surely a good one. One could make a very good evolutionary argument that more obvious methods of communication (e.g., bleating loudly) would have been detected by humans long ago, and that would be no good at all for the sheep.

Studies 2 and 3 further supported Zoltan’s story. Study 2 demonstrated that when you taped sheep’s ears to their heads, they ceased to communicate entirely. You could put Rozalia and Erzsebet in adjacent enclosures and show Rozalia the Jack of Spades for three or four minutes at a time, and when you went to test Erzsebet, she still wouldn’t know the Jack of Spades from the Three of Diamonds. It was as if the sheep were blind! Except they weren’t blind, they were dumb. Zoltan knew; he had made them that way by taping their ears to their heads.

In Study 3, Zoltan found that when the sheep’s eyes were covered, they no longer coordinated ear twitching. Instead, they now coordinated their bleating—but only if you excluded bleats that were produced when the sheep’s heads were oriented downwards. “Fantastic,” he thought. “When you cover their eyes, they can’t see each other’s ears any more. So they use a vocal channel. This, again, makes good adaptive sense: communication is too important to eliminate entirely just because your eyes happen to be covered. Much better to incur a small risk of being detected and make yourself known in other, less subtle, ways.”

But the real clincher was Study 4, which confirmed that ear twitching occurred at a higher rate in smaller groups than larger groups, and was particularly common in dyads of well-adjusted sheep (like Anastasia and Orsolya, and definitely not like Zsa Zsa and Marianna).

“Sheep are like everyday people,” Zoltan told his sister on the phone. “They won’t say anything to your face in public, but get them one-on-one, and they won’t stop gossiping about each other.”

It was a compelling story, Zoltan conceded to himself. The only problem was the F test. The difference in twitch rates as a function of group size wasn’t quite statistically significant. Instead, it hovered around p = .07, which the textbooks told Zoltan meant that he was almost right. Almost right was the same thing as potentially wrong, which wasn’t good enough. So the next morning, Zoltan asked Gergely to lend him four sheep so he could increase his sample size.

“Absolutely not,” said Gergely. “I don’t want your sheep filling my sheep’s heads with all of your crazy new ideas.”

“Look,” said Zoltan. “If you lend me four sheep, I’ll let you drive my Cadillac down to the village on weekends after I get famous.”

“Deal,” said Gergely.

So Zoltan borrowed the sheep. But it turned out that four sheep weren’t quite enough; after adding Gergely’s sheep to the sample, the effect only went from p < .07 to p < .06. So Zoltan cut a deal with his other neighbor, Yuri: four of Yuri’s sheep for two days, in return for three days with Zoltan’s new Lexus (once he bought it). That did the trick. Once Zoltan repeated the experiment with Yuri’s sheep, the p-value for Study 2 now came to .046, which the textbooks assured Zoltan meant he was going to be famous.

Data in hand, Zoltan spent the next two weeks writing up his very first journal article. He titled it “Baa baa baa, or not: Sheep communicate via non-verbal channels”—a decidedly modest title for the first empirical work to demonstrate that sheep are capable of sophisticated propositional thought. The article was published to widespread media attention and scientific acclaim, and Zoltan went on to have a productive few years in animal behavioral research, studying topics as interesting and varied as giraffe calisthenics and displays of affection in the common leech.

Much later, it turned out that no one was able to directly replicate his original findings with sheep (though some other researchers did manage to come up with conceptual replications). But that didn’t really matter to Zoltan, because by then he’d decided science was too demanding a career anyway; it was way more fun to lay under trees counting his sheep. Counting sheep, and occasionally, on Saturdays, driving down to the village in his new Lexus,  just to impress all the young cowgirls.