Tag: evaluation

Now I am become DOI, destroyer of gatekeeping worlds

Digital object identifiers (DOIs) are much sought-after commodities in the world of academic publishing. If you’ve never seen one, a DOI is a unique string associated with a particular digital object (most commonly a publication of some kind) that lets the internet know where to find the stuff you’ve written. For example, say you want to know where you can get a hold of an article titled, oh, say, Designing next-generation platforms for evaluating scientific output: what scientists can learn from the social web. In the real world, you’d probably go to Google, type that title in, and within three or four clicks, you’d arrive at the document you’re looking for. As it turns out, the world of formal resource location is fairly similar to the real world, except that instead of using Google, you go to a website called dx.DOI.org, and then you plug in the string ‘10.3389/fncom.2012.00072’, which is the DOI associated with the aforementioned article. And then, poof, you’re automagically linked directly to the original document, upon which you can gaze in great awe for as long as you feel comfortable.

Historically, DOIs have almost exclusively been issued by official-type publishers: Elsevier, Wiley, PLoS and such. Consequently, DOIs have had a reputation as a minor badge of distinction–probably because you’d traditionally only get one if your work was perceived to be important enough for publication in a journal that was (at least nominally) peer-reviewed. And perhaps because of this tendency to view the presence of a DOIs as something like an implicit seal of approval from the Great Sky Guild of Academic Publishing, many journals impose official or unofficial commandments to the effect that, when writing a paper, one shalt only citeth that which hath been DOI-ified. For example, here’s a boilerplate Elsevier statement regarding references (in this case, taken from the Neuron author guidelines):

References should include only articles that are published or in press. For references to in press articles, please confirm with the cited journal that the article is in fact accepted and in press and include a DOI number and online publication date. Unpublished data, submitted manuscripts, abstracts, and personal communications should be cited within the text only.

This seems reasonable enough until you realize that citations that occur “within the text only” aren’t very useful, because they’re ignored by virtually all formal citation indices. You want to cite a blog post in your Neuron paper and make sure it counts? Well, you can’t! Blog posts don’t have DOIs! You want to cite a what? A tweet? That’s just crazy talk! Tweets are 140 characters! You can’t possibly cite a tweet; the citation would be longer than the tweet itself!

The injunction against citing DOI-less documents is unfortunate, because people deserve to get credit for the interesting things they say–and it turns out that they have, on rare occasion, been known to say interesting things in formats other than the traditional peer-reviewed journal article. I’m pretty sure if Mark Twain were alive today, he’d write the best tweets EVER. Well, maybe it would be a tie between Mark Twain and the NIH Bear. But Mark Twain would definitely be up there. And he’d probably write some insightful blog posts too. And then, one imagines that other people would probably want to cite this brilliant 21st-century man of letters named @MarkTwain in their work. Only they wouldn’t be allowed to, you see, because 21st-century Mark Twain doesn’t publish all, or even most, of his work in traditional pre-publication peer-reviewed journals. He’s too impatient to rinse-and-repeat his way through the revise-and-resubmit process every time he wants to share a new idea with the world, even when those ideas are valuable. 21st-century @MarkTwain just wants his stuff out there already where people can see it.

Why does Elsevier hate 21st-century Mark Twain, you ask? I don’t know. But in general, I think there are two main reasons for the disdain many people seem to feel at the thought of allowing authors to freely cite DOI-less objects in academic papers. The first reason has to do with permanence—or lack thereof. The concern here is that if we allowed everyone to cite just any old web page, blog post, or tweet in academic articles, there would be no guarantee that those objects would still be around by the time the citing work was published, let alone several years hence. Which means that readers might be faced with a bunch of dead links. And dead links are not very good at backing up scientific arguments. In principle, the DOI requirement is supposed to act like some kind of safety word that protects a citation from the ravages of time—presumably because having a DOI means the cited work is important enough for the watchful eye of Sauron Elsevier to periodically scan across it and verify that it hasn’t yet fallen off of the internet’s cliffside.

The second reason has to do with quality. Here, the worry is that we can’t just have authors citing any old opinion someone else published somewhere on the web, because, well, think of the children! Terrible things would surely happen if we allowed authors to link to unverified and unreviewed works. What would stop me from, say, writing a paper criticizing the idea that human activity is contributing to climate change, and supporting my argument with “citations” to random pages I’ve found via creative Google searches? For that matter, what safeguard would prevent a brazen act of sockpuppetry in which I cite a bunch of pages that I myself have (anonymously) written? Loosening the injunction against formally citing non-peer-reviewed work seems tantamount to inviting every troll on the internet to a formal academic dinner.

To be fair, I think there’s some merit to both of these concerns. Or at least, I think there used to be some merit to these concerns. Back when the internet was a wee nascent flaky thing winking in and out of existence every time a dial-up modem connection went down, it made sense to worry about permanence (I mean, just think: if we had allowed people to cite GeoCities webpages in published articles, every last one of those citations links would now be dead!) And similarly, back in the days when peer review was an elite sort of activity that could only be practiced by dignified gentlepersons at the cordial behest of a right honorable journal editor, it probably made good sense to worry about quality control. But the merits of such concerns have now largely disappeared, because we now live in a world of marvelous technology, where bits of information cost virtually nothing to preserve forever, and a new post-publication platform that allows anyone to review just about any academic work in existence seems to pop up every other week (cf. PubPeer, PubMed Commons, Publons, etc.). In the modern world, nothing ever goes out of print, and if you want to know what a whole bunch of experts think about something, you just have to ask them about it on Twitter.

Which brings me to this blog post. Or paper. Whatever you want to call it. It was first published on my blog. You can find it–or at least, you could find it at one point in time–at the following URL: http://www.talyarkoni.org/blog/2015/03/04/now-i-am-become-doi-destroyer-of-gates.

Unfortunately, there’s a small problem with this URL: it contains nary a DOI in sight. Really. None of the eleventy billion possible substrings in it look anything like a DOI. You can even scramble the characters if you like; I don’t care. You’re still not going to find one. Which means that most journals won’t allow you to officially cite this blog post in your academic writing. Or any other post, for that matter. You can’t cite my post about statistical power and magical sample sizes; you can’t cite Joe Simmons’ Data Colada post about Mturk and effect sizes; you can’t cite Sanjay Srivastava’s discussion of replication and falsifiability; and so on ad infinitum. Which is a shame, because it’s a reasonably safe bet that there are at least one or two citation-worthy nuggets of information trapped in some of those blog posts (or millions of others), and there’s no reason to believe that these nuggets must all have readily-discoverable analogs somewhere in the “formal” scientific literature. As the Elsevier author guidelines would have it, the appropriate course of action in such cases is to acknowledge the source of an idea or finding in the text of the article, but not to grant any other kind of formal credit.

Now, typically, this is where the story would end. The URL can’t be formally cited in an Elsevier article; end of story. BUT! In this case, the story doesn’t quite end there. A strange thing happens! A short time after it appears on my blog, this post also appears–in virtually identical form–on something called The Winnower, which isn’t a blog at all, but rather, a respectable-looking alternative platform for scientific publication and evaluation.

Even more strangely, on The Winnower, a mysterious-looking set of characters appear alongside the text. For technical reasons, I can’t tell you what the set of characters actually is (because it isn’t assigned until this piece is published!). But I can tell you that it starts with “10.15200/winn”. And I can also tell you what it is: It’s a DOI! It’s one bona fide free DOI, courtesy of The Winnower. I didn’t have to pay for it, or barter any of my services for it, or sign away any little pieces of my soul to get it*. I just installed a WordPress plugin, pressed a few buttons, and… poof, instant DOI. So now this is, proudly, one of the world’s first N (where N is some smallish number probably below 1000) blog posts to dress itself up in a nice DOI (Figure 1). Presumably because it’s getting ready for a wild night out on the academic town.

sticks and stones may break my bones, but DOIs make me feel pretty
Figure 1. Effects of assigning DOIs to blog posts: an anthropomorphic depiction. (A) A DOI-less blog post feels exposed and inadequate; it envies its more reputable counterparts and languishes in a state of torpor and existential disarray. (B) Freshly clothed in a newly-minted DOI, the same blog post feels confident, charismatic, and alert. Brimming with energy, it eagerly awaits the opportunity to move mountains and reshape scientific discourse. Also, it has longer arms.

Does the mere fact that my blog post now has a DOI actually change anything, as far as the citation rules go? I don’t know. I have no idea if publishers like Elsevier will let you officially cite this piece in an article in one of their journals. I would guess not, but I strongly encourage you to try it anyway (in fact, I’m willing to let you try to cite this piece in every paper you write for the next year or so—that’s the kind of big-hearted sacrifice I’m willing to make in the name of science). But I do think it solves both the permanence and quality control issues that are, in theory, the whole reason for journals having a no-DOI-no-shoes-no-service policy in the first place.

How? Well, it solves the permanence problem because The Winnower is a participant in the CLOCKSS archive, which means that if The Winnower ever goes out of business (a prospect that, let’s face it, became a little bit more likely the moment this piece appeared on their site), this piece will be immediately, freely, and automatically made available to the worldwide community in perpetuity via the associated DOI. So you don’t need to trust the safety of my blog—or even The Winnower—any more. This piece is here to stay forever! Rejoice in the cheapness of digital information and librarians’ obsession with archiving everything!

As for the quality argument, well, clearly, this here is not what you would call a high-quality academic work. But I still think you should be allowed to cite it wherever and whenever you want. Why? For several reasons. First, it’s not exactly difficult to determine whether or not it’s a high-quality academic work—even if you’re not willing to exercise your own judgment. When you link to a publication on The Winnower, you aren’t just linking to a paper; you’re also linking to a review platform. And the reviews are very prominently associated with the paper. If you dislike this piece, you can use the comment form to indicate exactly why you dislike it (if you like it, you don’t need to write a comment; instead, send an envelope stuffed with money to my home address).

Second, it’s not at all clear that banning citations to non-prepublication-reviewed materials accomplishes anything useful in the way of quality control. The reliability of the peer-review process is sufficiently low that there is simply no way for it to consistently sort the good from the bad. The problem is compounded by the fact that rejected manuscripts are rarely discarded forever; typically, they’re quickly resubmitted to another journal. The bibliometric literature shows that it’s possible to publish almost anything in the peer-reviewed literature given enough persistence.

Third, I suspect—though I have no data to support this claim—that a worldview that treats having passed peer review and/or receiving a DOI as markers of scientific quality is actually counterproductive to scientific progress, because it promotes a lackadaisical attitude on the part of researchers. A reader who believes that a claim is significantly more likely to be true in virtue of having a DOI is a reader who is slightly less likely to take the extra time to directly evaluate the evidence for that claim. The reality, unfortunately, is that most scientific claims are wrong, because the world is complicated and science is hard. Pretending that there is some reasonably accurate mechanism that can sort all possible sources into reliable and unreliable buckets—even to a first order of approximation—is misleading at best and dangerous at worst. Of course, I’m not suggesting that you can’t trust a paper’s conclusions unless you’ve read every work it cites in detail (I don’t believe I’ve ever done that for any paper!). I’m just saying that you can’t abdicate the responsibility of evaluating the evidence to some shapeless, anonymous mass of “reviewers”. If I decide not to chase down the Smith & Smith (2007) paper that Jones & Jones (2008) cite as critical support for their argument, I shouldn’t be able to turn around later and say something like “hey, Smith & Smith (2007) was peer reviewed, so it’s not my fault for not bothering to read it!”

So where does that leave us? Well, if you’ve read this far, and agree with most or all of the above arguments, I hope I can convince you of one more tiny claim. Namely, that this piece represents (a big part of) the future of academic publishing. Not this particular piece, of course; I mean the general practice of (a) assigning unique identifiers to digital objects, (b) preserving those objects for all posterity in a centralized archive, and (c) allowing researchers to cite any and all such objects in their work however they like. (We could perhaps also add (d) working very hard to promote centralized “post-publication” peer review of all of those objects–but that’s a story for another day.)

These are not new ideas, mind you. People have been calling for a long time for a move away from a traditional gatekeeping-oriented model of pre-publication review and towards more open publication and evaluation models. These calls have intensified in recent years; for instance, in 2012, a special topic in Frontiers in Computational Neuroscience featured 18 different papers that all independently advocated for very similar post-publication review models. Even the actual attachment of DOIs to blog posts isn’t new; as a case in point, consider that C. Titus Brown—in typical pioneering form—was already experimenting with ways to automatically DOIfy his blog posts via FigShare way back in the same dark ages of 2012. What is new, though, is the emergence and widespread adoption of platforms like The Winnower, FigShare, or Research Gate that make it increasingly easy to assign a DOI to academically-relevant works other than traditional journal articles. Thanks to such services, you can now quickly and effortlessly attach a DOI to your open-source software packages, technical manuals and white papers, conference posters, or virtually any other kind of digital document.

Once such efforts really start to pick up steam—perhaps even in the next two or three years—I think there’s a good chance we’ll fall into a positive feedback loop, because it will become increasingly clear that for many kinds of scientific findings or observations, there’s simply nothing to be gained by going through the cumbersome, time-consuming conventional peer review process. To the contrary, there will be all kinds of incentives for researchers to publish their work as soon as they feel it’s ready to share. I mean, look, I can write blog posts a lot faster than I can write traditional academic papers. Which means that if I write, say, one DOI-adorned blog post a month, my Google Scholar profile is going to look a lot bulkier a year from now, at essentially no extra effort or cost (since I’m going to write those blog posts anyway!). In fact, since services like The Winnower and FigShare can assign DOIs to documents retroactively, you might not even have to wait that long. Check back this time next week, and I might have a dozen new indexed publications! And if some of these get cited—whether in “real” journals or on other indexed blog posts—they’ll then be contributing to my citation count and h-index too (at least on Google Scholar). What are you going to do to keep up?

Now, this may all seem a bit off-putting if you’re used to thinking of scientific publication as a relatively formal, laborious process, where two or three experts have to sign off on what you’ve written before it gets to count for anything. If you’ve grown comfortable with the idea that there are “real” scientific contributions on the one hand, and a blooming, buzzing confusion of second-rate opinions on the other, you might find the move to suddenly make everything part of the formal record somewhat disorienting. It might even feel like some people (like, say, me) are actively trying to game the very system that separates science from tabloid news. But I think that’s the wrong perspective. I don’t think anybody—certainly not me—is looking to get rid of peer review. What many people are actively working towards are alternative models of peer review that will almost certainly work better.

The right perspective, I would argue, is to embrace the benefits of technology and seek out new evaluation models that emphasize open, collaborative review by the community as a whole instead of closed pro forma review by two or three semi-randomly selected experts. We now live in an era where new scientific results can be instantly shared at essentially no cost, and where sophisticated collaborative filtering algorithms and carefully constructed reputation systems can potentially support truly community-driven, quantitatively-grounded open peer review on a massive scale. In such an environment, there are few legitimate excuses for sticking with archaic publication and evaluation models—only the familiar, comforting pull of the status quo. Viewed in this light, using technology to get around the limitations of old gatekeeper-based models of scientific publication isn’t gaming the system; it’s actively changing the system—in ways that will ultimately benefit us all. And in that context, the humble self-assigned DOI may ultimately become—to liberally paraphrase Robert Oppenheimer and the Bhagavad Gita—one of the destroyers of the old gatekeeping world.

Big Pitch or Big Lottery? The unenviable task of evaluating the grant review system

This week’s issue of Science has an interesting article on The Big Pitch–a pilot NSF initiative to determine whether anonymizing proposals and dramatically cutting down their length (from 15 pages to 2) has a substantial impact on the results of the review process. The answer appears to be an unequivocal yes. From the article:

What happens is a lot, according to the first two rounds of the Big Pitch. NSF’s grant reviewers who evaluated short, anonymized proposals picked a largely different set of projects to fund compared with those chosen by reviewers presented with standard, full-length versions of the same proposals.

Not surprisingly, the researchers who did well under the abbreviated format are pretty pleased:

Shirley Taylor, an awardee during the evolution round of the Big Pitch, says a comparison of the reviews she got on the two versions of her proposal convinced her that anonymity had worked in her favor. An associate professor of microbiology at Virginia Commonwealth University in Richmond, Taylor had failed twice to win funding from the National Institutes of Health to study the role of an enzyme in modifying mitochondrial DNA.

Both times, she says, reviewers questioned the validity of her preliminary results because she had few publications to her credit. Some reviews of her full proposal to NSF expressed the same concern. Without a biographical sketch, Taylor says, reviewers of the anonymous proposal could “focus on the novelty of the science, and this is what allowed my proposal to be funded.”

Broadly speaking, there are two ways to interpret the divergent results of the standard and abbreviated review. The charitable interpretation is that the change in format is, in fact, beneficial, inasmuch as it eliminates prior reputation as one source of bias and forces reviewers to focus on the big picture rather than on small methodological details. Of course, as Prof-Like Substance points out in an excellent post, one could mount a pretty reasonable argument that this isn’t necessarily a good thing. After all, a scientist’s past publication record is likely to be a good predictor of their future success, so it’s not clear that proposals should be anonymous when large amounts of money are on the line (and there are other ways to counteract the bias against newbies–e.g., NIH’s approach of explicitly giving New Investigators a payline boost until they get their first R01). And similarly, some scientists might be good at coming up with big ideas that sound plausible at first blush and not so good at actually carrying out the research program required to bring those big ideas to fruition. Still, at the very least, if we’re being charitable, The Big Pitch certainly does seem like a very different kind of approach to review.

The less charitable interpretation is that the reason the ratings of the standard and abbreviated proposals showed very little correlation is that the latter approach is just fundamentally unreliable. If you suppose that it’s just not possible to reliably distinguish a very good proposal from a somewhat good one on the basis of just 2 pages, it makes perfect sense that 2-page and 15-page proposal ratings don’t correlate much–since you’re basically selecting at random in the 2-page case. Understandably, researchers who happen to fare well under the 2-page format are unlikely to see it that way; they’ll probably come up with many plausible-sounding reasons why a shorter format just makes more sense (just like most researchers who tend to do well with the 15-page format probably think it’s the only sensible way for NSF to conduct its business). We humans are all very good at finding self-serving rationalizations for things, after all.

Personally I don’t have very strong feelings about the substantive merits of short versus long-format review–though I guess I do find it hard to believe that 2-page proposals could be ranked very reliably given that some very strange things seem to happen with alarming frequency even with 12- and 15-page proposals. But it’s an empirical question, and I’d love to see relevant data. In principle, the NSF could have obtained that data by having two parallel review panels rate all of the 2-page proposals (or even 4 panels, since one would also like to know how reliable the normal review process is). That would allow the agency to directly quantify the reliability of the ratings by looking at their cross-panel consistency. Absent that kind of data, it’s very hard to know whether the results Science reports on are different because 2-page review emphasizes different (but important) things, or because a rating process based on an extended 2-page abstract just amounts to a glorified lottery.

Alternatively, and perhaps more pragmatically, NSF could just wait a few years to see how the projects funded under the pilot program turn out (and I’m guessing this is part of their plan). I.e., do the researchers who do well under the 2-page format end producing science as good as (or better than) the researchers who do well under the current system? This sounds like a reasonable approach in principle, but the major problem is that we’re only talking about a total of ~25 funded proposals (across two different review panels), so it’s unclear that there will be enough data to draw any firm conclusions. Certainly many scientists (including me) are likely to feel a bit uneasy at the thought that NSF might end up making major decisions about how to allocate billions of dollars on the basis of two dozen grants.

Anyway, skepticism aside, this isn’t really meant as a criticism of NSF so much as an acknowledgment of the fact that the problem in question is a really, really difficult one. The task of continually evaluating and improving the grant review process is not one anyone should want to take on lightly. If time and money were no object, every proposed change (like dramatically shortened proposals) would be extensively tested on a large scale and directly compared to the current approach before being implemented. Unfortunately, flying thousands of scientists to Washington D.C. is a very expensive business (to say nothing of all the surrounding costs), and I imagine that testing out a substantively different kind of review process on a large scale could easily run into the tens of millions of dollars. In a sense, the funding agencies can’t really win. On the one hand, if they only ever pilot new approaches on a small scale, they never get enough empirical data to confidently back major changes in policy. On the other hand, if they pilot new approaches on a large scale and those approaches end up failing to improve on the current system (as is the fate of most innovative new ideas), the funding agencies get hammered by politicians and scientists alike for wasting taxpayer money in an already-harsh funding climate.

I don’t know what the solution is (or if there is one), but if nothing else, I do think it’s a good thing that NSF and NIH continue to actively tinker with their various processes. After all, if there’s anything most researchers can agree on, it’s that the current system is very far from perfect.

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?