Month: February 2011

what Paul Meehl might say about graduate school admissions

Sanjay Srivastava has an excellent post up today discussing the common belief among many academics (or at least psychologists) that graduate school admission interviews aren’t very predictive of actual success, and should be assigned little or no weight when making admissions decisions:

The argument usually goes something like this: “All the evidence from personnel selection studies says that interviews don’t predict anything. We are wasting people’s time and money by interviewing grad students, and we are possibly making our decisions worse by substituting bad information for good.“

I have been hearing more or less that same thing for years, starting when I was grad school myself. In fact, I have heard it often enough that, not being familiar with the literature myself, I accepted what people were saying at face value. But I finally got curious about what the literature actually says, so I looked it up.

I confess that I must have been drinking from the kool-aid spigot, because until I read Sanjay’s post, I’d long believed something very much like this myself, and for much the same reason. I’d never bothered to actually, you know, look at the data myself. Turns out the evidence and the kool-aid are not compatible:

A little Google Scholaring for terms like “employment interviews“ and “incremental validity“ led me to a bunch of meta-analyses that concluded that in fact interviews can and do provide useful information above and beyond other valid sources of information (like cognitive ability tests, work sample tests, conscientiousness, etc.). One of the most heavily cited is a 1998 Psych Bulletin paper by Schmidt and Hunter (link is a pdf; it’s also discussed in this blog post). Another was this paper by Cortina et al, which makes finer distinctions among different kinds of interviews. The meta-analyses generally seem to agree that (a) interviews correlate with job performance assessments and other criterion measures, (b) interviews aren’t as strong predictors as cognitive ability, (c) but they do provide incremental (non-overlapping) information, and (d) in those meta-analyses that make distinctions between different kinds of interviews, structured interviews are better than unstructured interviews.

This seems entirely reasonable, and I agree with Sanjay that it clearly shows that admissions interviews aren’t useless, at least in an actuarial sense. That said, after thinking about it for a while, I’m not sure these findings really address the central question admissions committees care about. When deciding which candidates to admit as students, the relevant question isn’t really what factors predict success in graduate school?, it’s what factors should the admissions committee attend to when making a decision? These may seem like the same thing, but they’re not. And the reason they’re not is that knowing which factors are predictive of success is no guarantee that faculty are actually going to be able to use that information in an appropriate way. Knowing what predicts performance is only half the story, as it were; you also need to know exactly how to weight different factors appropriately in order to generate an optimal prediction.

In practice, humans turn out to be incredibly bad at predicting outcomes based on multiple factors. An enormous literature on mechanical (or actuarial) prediction, which Sanjay mentions in his post, has repeatedly demonstrated that in many domains, human judgments are consistently and often substantially outperformed by simple regression equations. There are several reasons for this gap, but one of the biggest ones is that people are just shitty at quantitatively integrating multiple continuous variables. When you visit a car dealership, you may very well be aware that your long-term satisfaction with any purchase is likely to depend on some combination of horsepower, handling, gas mileage, seating comfort, number of cupholders, and so on. But the odds that you’ll actually be able to combine that information in an optimal way are essentially nil. Our brains are simply not designed to work that way; you can’t internally compute the value you’d get out of a car using an equation like 1.03*cupholders + 0.021*horsepower + 0.3*mileage. Some of us try to do it that way–e.g., by making very long pro and con lists detailing all the relevant factors we can possibly think of–but it tends not to work out very well (e.g., you total up the numbers and realize, hey, that’s not the answer I wanted! And then you go buy that antique ’68 Cadillac you had your eye on the whole time you were pretending to count cupholders in the Nissan Maxima).

Admissions committees face much the same problem. The trouble lies not so much in determining which factors predict graduate school success (or, for that matter, many other outcomes we care about in daily life), but in determining how to best combine them. Knowing that interview performance incrementally improves predictions is only useful if you can actually trust decision-makers to weight that variable very lightly relative to other more meaningful predictors like GREs and GPAs. And that’s a difficult proposition, because I suspect that admissions discussions rarely go like this:

Faculty Member 1: I think we should accept Candidate X. Her GREs are off the chart, great GPA, already has two publications.
Faculty Member 2: I didn’t like X at all. She didn’t seem very excited to be here.
FM1: Well, that doesn’t matter so much. Unless you really got a strong feeling that she wouldn’t stick it out in the program, it probably won’t make much of a difference, performance-wise.
FM2: Okay, fine, we’ll accept her.

And more often go like this:

FM1: Let’s take Candidate X. Her GREs are off the chart, great GPA, already has two publications.
FM2: I didn’t like X at all. She didn’t seem very excited to be here.
FM1: Oh, you thought so too? That’s kind of how I felt too, but I didn’t want to say anything.
FM2: Okay, we won’t accept X. We have plenty of other good candidates with numbers that are nearly as good and who seemed more pleasant.

Admittedly, I don’t have any direct evidence to back up this conjecture. Except that I think it would be pretty remarkable if academic faculty departed from experts in pretty much every other domain that’s been tested (clinical practice, medical diagnosis, criminal recidivism, etc.) and were actually able to do as well (or even close to as well) as a simple regression equation. For what it’s worth, in many of the studies of mechanical prediction, the human experts are explicitly given all of the information passed to the prediction equation, and still do relatively poorly. In other words, you can hand a clinical psychologist a folder full of quantitative information about a patient, tell them to weight it however they want, and even the best clinicians are still going to be outperformed by a mechanical prediction (if you doubt this to be true, I second Sanjay in directing you to Paul Meehl’s seminal body of work–truly some of the most important and elegant work ever done in psychology, and if you haven’t read it, you’re missing out). And in some sense, faculty members aren’t really even experts about admissions, since they only do it once a year. So I’m pretty skeptical that admissions committees actually manage to weight their firsthand personal experience with candidates appropriately when making their final decisions. It seems much more likely that any personality impressions they come away with will just tend to drown out prior assessments based on (relatively) objective data.

That all said, I couldn’t agree more with Sanjay’s ultimate conclusion, so I’ll just end with this quote:

That, of course, is a testable question. So if you are an evidence-based curmudgeon, you should probably want some relevant data. I was not able to find any studies that specifically addressed the importance of rapport and interest-matching as predictors of later performance in a doctoral program. (Indeed, validity studies of graduate admissions are few and far between, and the ones I could find were mostly for medical school and MBA programs, which are very different from research-oriented Ph.D. programs.) It would be worth doing such studies, but not easy.

Oh, except that I do want to add that I really like the phrase “evidence-based curmudgeon“, and I’m totally stealing it.

some people are irritable, but everyone likes to visit museums: what personality inventories tell us about how we’re all just like one another

I’ve recently started recruiting participants for online experiments via Mechanical Turk. In the past I’ve always either relied on on directory listings (like this one) or targeted specific populations (e.g., bloggers and twitterers) via email solicitation. But recently I’ve started running a very large-sample decision-making study (it’s here, if you care to contribute to the sample), and waiting for participants to trickle in via directories isn’t cutting it. So I’ve started paying people (very) small amounts of money for participation.

One challenge I’ve had to deal with is figuring out how to filter out participants who aren’t really interested in contributing to science, and are strictly in it for the money. 20 or 30 cents is a pittance to most people in the developed world, but as I’ve found out the hard way, gaming MTurk appears to be a thriving business in some developing countries (some of which I’ve unfortunately had to resort to banning entirely). Cheaters aren’t so much of an issue for very quick tasks like providing individual ratings of faces, because (a) the time it takes to give a fake rating isn’t substantially greater than giving one’s actual opinion, and (b) the standards for what counts as accurate performance are clear, so it’s easy to train workers and weed out the bad apples. Unfortunately, my studies generally involve fairly long personality questionnaires combined with other cognitive tasks (e.g., in the current study, you get to repeatedly allocate hypothetical money between yourself and a computer partner, and rate some faces). They often take around half an hour, and involve 20+ questions per screen, so there’s a pretty big incentive for workers who are only in it for the cash to produce random responses and try to increase their effective wage. And the obvious question then is how to detect cheating in the data.

One of the techniques I’ve found works surprisingly well is to simply compare each person’s pattern of responses across items with the mean for the entire sample. In other words, you just compute the correlation between each individual’s item scores and the means for all the items scores across everyone who’s filled out the same measure. I know that there’s an entire literature on this stuff full of much more sophisticated ways to detect random responding, but I find this crude approach really does quite well (I’ve verified this by comparing it with a bunch of other similar metrics), and has the benefit of being trivial to implement.

Anyway, one of the things that surprised me when I first computed these correlations is just how strong the relationship between the sample mean and most individuals’ responses is. Here’s what the distribution looks like for one particular inventory, the 181-item Analog to Multiple Broadband Inventories (AMBI, whichI introduced in this paper, and discuss further here):

This is based on a sample of about 600 internet respondents, which actually turns out to be pretty representative of the broader population, as Sam Gosling, Simine Vazire, and Sanjay Srivastava will tell you (for what it’s worth, I’ve done the exact same analysis on a similar-sized off-line dataset from Lew Goldberg’s Eugene-Springfield Community Sample (check out that URL!) and obtained essentially the same results). In this sample, the median correlation is .48; so, in effect, you can predict a quarter of the variance in a typical participant’s responses without knowing anything at all about them. Human beings, it turns out, have some things in common with one another (who knew?). What you think you’re like is probably not very dissimilar to what I think I’m like. Which is kind of surprising, considering you’re a well-adjusted, friendly human being, and I’m a real freakshow somewhat eccentric, paranoid kind of guy.

What drives that similarity? Much of it probably has to do with social desirability–i.e., many of the AMBI items (and those on virtually all personality inventories) are evaluatively positive or negative statements that most people are inclined to strongly agree or disagree with. But it seems to be a particular kind of social desirability–one that has to do with openness to new experiences, and particular intellectual ones. For instance, here are the top 10 most endorsed items (based on mean likert scores across the entire sample; scores are in parentheses):

  1. like to read (4.62)
  2. like to visit new places (4.39)
  3. was a better than average student when I was in school (4.28)
  4. am a good listener (4.25)
  5. would love to explore strange places (4.22)
  6. am concerned about others (4.2)
  7. am open to new experiences (4.18)
  8. amuse my friends (4.16)
  9. love excitement (4.08)
  10. spend a lot of time reading (4.07)

And conversely, here are the 10 least-endorsed items:

  1. was a slow learner in school (1.52)
  2. don’t think that laws apply to me (1.8)
  3. do not like to visit museums (1.83)
  4. have difficulty imagining things (1.84)
  5. have no special urge to do something original (1.87)
  6. do not like art (1.95)
  7. feel little concern for others (1.97)
  8. don’t try to figure myself out (2.01)
  9. break my promises (2.01)
  10. make enemies (2.06)

You can see a clear evaluative component in both lists: almost everyone believes that they’re concerned about others and thinks that they’re smarter than average. But social desirability and positive illusions aren’t enough to explain these patterns, because there are plenty of other items on the AMBI that have an equally strong evaluative component–for instance, “don’t have much energy”, “cannot imagine lying or cheating”, “see myself as a good leader”, and “am easily annoyed”–yet have mean scores pretty close to the midpoint (in fact, the item ‘am easily annoyed’ is endorsed more highly than 107 of the 181 items!). So it isn’t just that we like to think and say nice things about ourselves; we’re willing to concede that we have some bad traits, but maybe not the ones that have to do with disliking cultural and intellectual experiences. I don’t have much of an idea as to why that might be, but it does introspectively feel to me like there’s more of a stigma about, say, not liking to visit new places or experience new things than admitting that you’re kind of an irritable person. Or maybe it’s just that many of the openness items can be interpreted more broadly than the other evaluative items–e.g., there are lots of different art forms, so almost everyone can endorse a generic “I like art” statement. I don’t really know.

Anyway, there’s nothing the least bit profound about any of this; if anything, it’s just a nice reminder that most of us are not really very good at evaluating where we stand in relation to other people, at least for many traits (for more on that, go read Simine Vazire’s work). The nominal midpoint on most personality scales is usually quite far from the actual median in the general population. This is a pretty big challenge for personality psychology, and if we could figure out how to get people to rank themselves more accurately relative to other people on self-report measures, that would be a pretty huge advance. But it seems quite likely that you just can’t do it, because people simply may not have introspective access to that kind of information.

Fortunately for our ability to measure individual differences in personality, there are plenty of items that do show considerable variance across individuals (actually, in fairness, even items with relatively low variance like the ones above can be highly discriminative if used properly–that’s what item response theory is for). Just for kicks, here are the 10 AMBI items with the largest standard deviations (in parentheses):

  1. disliked math in school (1.56)
  2. wanted to run away from home when I was a child (1.56)
  3. believe in a universal power or god (1.53)
  4. have felt contact with a divine power (1.51)
  5. rarely cry during sad movies (1.46)
  6. am able to fix electrical-wiring problems (1.46)
  7. am devoted to religion (1.44)
  8. shout or scream when I’m angry (1.43)
  9. love large parties (1.42)
  10. felt close to my parents when I was a child (1.42)

So now finally we come to the real moral of this post… that which you’ve read all this long way for. And the moral is this, grasshopper: if you want to successfully pick a fight at a large party, all you need to do is angrily yell at everyone that God told you math sucks.

Too much p = .048? Towards partial automation of scientific evaluation

Distinguishing good science from bad science isn’t an easy thing to do. One big problem is that what constitutes ‘good’ work is, to a large extent, subjective; I might love a paper you hate, or vice versa. Another problem is that science is a cumulative enterprise, and the value of each discovery is, in some sense, determined by how much of an impact that discovery has on subsequent work–something that often only becomes apparent years or even decades after the fact. So, to an uncomfortable extent, evaluating scientific work involves a good deal of guesswork and personal preference, which is probably why scientists tend to fall back on things like citation counts and journal impact factors as tools for assessing the quality of someone’s work. We know it’s not a great way to do things, but it’s not always clear how else we could do better.

Fortunately, there are many aspects of scientific research that don’t depend on subjective preferences or require us to suspend judgment for ten or fifteen years. In particular, methodological aspects of a paper can often be evaluated in a (relatively) objective way, and strengths or weaknesses of particular experimental designs are often readily discernible. For instance, in psychology, pretty much everyone agrees that large samples are generally better than small samples, reliable measures are better than unreliable measures, representative samples are better than WEIRD ones, and so on. The trouble when it comes to evaluating the methodological quality of most work isn’t so much that there’s rampant disagreement between reviewers (though it does happen), it’s that research articles are complicated products, and the odds of any individual reviewer having the expertise, motivation, and attention span to catch every major methodological concern in a paper are exceedingly small. Since only two or three people typically review a paper pre-publication, it’s not surprising that in many cases, whether or not a paper makes it through the review process depends as much on who happened to review it as on the paper itself.

A nice example of this is the Bem paper on ESP I discussed here a few weeks ago. I think most people would agree that things like data peeking, lumping and splitting studies, and post-hoc hypothesis testing–all of which are apparent in Bem’s paper–are generally not good research practices. And no doubt many potential reviewers would have noted these and other problems with Bem’s paper had they been asked to reviewer. But as it happens, the actual reviewers didn’t note those problems (or at least, not enough of them), so the paper was accepted for publication.

I’m not saying this to criticize Bem’s reviewers, who I’m sure all had a million other things to do besides pore over the minutiae of a paper on ESP (and for all we know, they could have already caught many other problems with the paper that were subsequently addressed before publication). The problem is a much more general one: the pre-publication peer review process in psychology, and many other areas of science, is pretty inefficient and unreliable, in the sense that it draws on the intense efforts of a very few, semi-randomly selected, individuals, as opposed to relying on a much broader evaluation by the community of researchers at large.

In the long term, the best solution to this problem may be to fundamentally rethink the way we evaluate scientific papers–e.g., by designing new platforms for post-publication review of papers (e.g., see this post for more on efforts towards that end). I think that’s far and away the most important thing the scientific community could do to improve the quality of scientific assessment, and I hope we ultimately will collectively move towards alternative models of review that look a lot more like the collaborative filtering systems found on, say, reddit or Stack Overflow than like peer review as we now know it. But that’s a process that’s likely to take a long time, and I don’t profess to have much of an idea as to how one would go about kickstarting it.

What I want to focus on here is something much less ambitious, but potentially still useful–namely, the possibility of automating the assessment of at least some aspects of research methodology. As I alluded to above, many of the factors that help us determine how believable a particular scientific finding is are readily quantifiable. In fact, in many cases, they’re already quantified for us. Sample sizes, p values, effect sizes,  coefficient alphas… all of these things are, in one sense or another, indices of the quality of a paper (however indirect), and are easy to capture and code. And many other things we care about can be captured with only slightly more work. For instance, if we want to know whether the authors of a paper corrected for multiple comparisons, we could search for strings like “multiple comparisons”, “uncorrected”, “Bonferroni”, and “FDR”, and probably come away with a pretty decent idea of what the authors did or didn’t do to correct for multiple comparisons. It might require a small dose of technical wizardry to do this kind of thing in a sensible and reasonably accurate way, but it’s clearly feasible–at least for some types of variables.

Once we extracted a bunch of data about the distribution of p values and sample sizes from many different papers, we could then start to do some interesting (and potentially useful) things, like generating automated metrics of research quality. For instance:

  • In multi-study articles, the variance in sample size across studies could tell us something useful about the likelihood that data peeking is going on (for an explanation as to why, see this). Other things being equal, an article with 9 studies with identical sample sizes is less likely to be capitalizing on chance than one containing 9 studies that range in sample size between 50 and 200 subjects (as the Bem paper does), so high variance in sample size could be used as a rough index for proclivity to peek at the data.
  • Quantifying the distribution of p values found in an individual article or an author’s entire body of work might be a reasonable first-pass measure of the amount of fudging (usually inadvertent) going on. As I pointed out in my earlier post, it’s interesting to note that with only one or two exceptions, virtually all of Bem’s statistically significant results come very close to p = .05. That’s not what you expect to see when hypothesis testing is done in a really principled way, because it’s exceedingly unlikely to think a researcher would be so lucky as to always just barely obtain the expected result. But a bunch of p = .03 and p = .048 results are exactly what you expect to find when researchers test multiple hypotheses and report only the ones that produce significant results.
  • The presence or absence of certain terms or phrases is probably at least slightly predictive of the rigorousness of the article as a whole. For instance, the frequent use of phrases like “cross-validated”, “statistical power”, “corrected for multiple comparisons”, and “unbiased” is probably a good sign (though not necessarily a strong one); conversely, terms like “exploratory”, “marginal”, and “small sample” might provide at least some indication that the reported findings are, well, exploratory.

These are just the first examples that come to mind; you can probably think of other better ones. Of course, these would all be pretty weak indicators of paper (or researcher) quality, and none of them are in any sense unambiguous measures. There are all sorts of situations in which such numbers wouldn’t mean much of anything. For instance, high variance in sample sizes would be perfectly justifiable in a case where researchers were testing for effects expected to have very different sizes, or conducting different kinds of statistical tests (e.g., detecting interactions is much harder than detecting main effects, and so necessitates larger samples). Similarly, p values close to .05 aren’t necessarily a marker of data snooping and fishing expeditions; it’s conceivable that some researchers might be so good at what they do that they can consistently design experiments that just barely manage to show what they’re intended to (though it’s not very plausible). And a failure to use terms like “corrected”, “power”, and “cross-validated” in a paper doesn’t necessarily mean the authors failed to consider important methodological issues, since such issues aren’t necessarily relevant to every single paper. So there’s no question that you’d want to take these kinds of metrics with a giant lump of salt.

Still, there are several good reasons to think that even relatively flawed automated quality metrics could serve an important purpose. First, many of the problems could be overcome to some extent through aggregation. You might not want to conclude that a particular study was poorly done simply because most of the reported p values were very close to .05; but if you were look at a researcher’s entire body of, say, thirty or forty published articles, and noticed the same trend relative to other researchers, you might start to wonder. Similarly, we could think about composite metrics that combine many different first-order metrics to generate a summary estimate of a paper’s quality that may not be so susceptible to contextual factors or noise. For instance, in the case of the Bem ESP article, a measure that took into account the variance in sample size across studies, the closeness of the reported p values to .05, the mention of terms like ‘one-tailed test’, and so on, would likely not have assigned Bem’s article a glowing score, even if each individual component of the measure was not very reliable.

Second, I’m not suggesting that crude automated metrics would replace current evaluation practices; rather, they’d be used strictly as a complement. Essentially, you’d have some additional numbers to look at, and you could choose to use them or not, as you saw fit, when evaluating a paper. If nothing else, they could help flag potential issues that reviewers might not be spontaneously attuned to. For instance, a report might note the fact that the term “interaction” was used several times in a paper in the absence of “main effect,” which might then cue a reviewer to ask, hey, why you no report main effects? — but only if they deemed it a relevant concern after looking at the issue more closely.

Third, automated metrics could be continually updated and improved using machine learning techniques. Given some criterion measure of research quality, one could systematically train and refine an algorithm capable of doing a decent job recapturing that criterion. Of course, it’s not clear that we really have any unobjectionable standard to use as a criterion in this kind of training exercise (which only underscores why it’s important to come up with better ways to evaluate scientific research). But a reasonable starting point might be to try to predict replication likelihood for a small set of well-studied effects based on the features of the original report. Could you for instance show, in an automated way, that initial effects reported in studies that failed to correct for multiple comparisons or reported p values closer to .05 were less likely to be subsequently replicated?

Of course, as always with this kind of stuff, the rub is that it’s easy to talk the talk and not so easy to walk the walk. In principle, we can make up all sorts of clever metrics, but in practice, it’s not trivial to automatically extract even a piece of information as seemingly simple as sample size from many papers (consider the difference between “Undergraduates (N = 15) participated…” and “Forty-two individuals diagnosed with depression and an equal number of healthy controls took part…”), let alone build sophisticated composite measures that could reasonably well approximate human judgments. It’s all well and good to write long blog posts about how fancy automated metrics could help separate good research from bad, but I’m pretty sure I don’t want to actually do any work to develop them, and you probably don’t either. Still, the potential benefits are clear, and it’s not like this is science fiction–it’s clearly viable on at least a modest scale. So someone should do it… Maybe Elsevier? Jorge Hirsch? Anyone? Bueller? Bueller?