Breathless headline-grabbing press releases based on modest findings. Investigations driven by confirmation bias. Broad generalizations based on tiny samples.
I am talking, of course, about the final report of the Diederik Stapel investigation.
Regular readers of my blog will know that I have been beating the drum for reform for quite a while. I absolutely think psychology in general, and perhaps social psychology especially, can and must work to improve its methods and practices.
But in reading the commission’s press release, which talks about “a general culture of careless, selective and uncritical handling of research and data” in social psychology, I am struck that those conclusions are based on a retrospective review of a known fraud case — a case that the commissions were specifically charged with finding an explanation for. So when they wag their fingers about a field rife with elementary statistical errors and confirmation bias, it’s a bit much for me.
I am writing this as a first reaction based on what I’ve seen in the press. At some point when I have the time and the stomach I plan to dig into the full 100-page commission report. I hope that — as is often the case when you go from a press release to an actual report — it takes a more sober and cautious tone. Because I do think that we have the potential to learn some important things by studying how Diederik Stapel did what he did. Most likely we will learn what kinds of hard questions we need to be asking of ourselves — not necessarily what the answers to those questions will be. Remember that the more we are shocked by the commission’s report, the less willing we should be to reach any sweeping generalizations from it.
So let’s all take a deep breath, face up to the Stapel case for what it is — neither exaggerating nor minimizing it — and then try to have a productive conversation about where we need to go next.
The tools we have available to us affect the way we interact with and even think about the world. “If all you have is a hammer” etc. Along these lines, I’ve been wondering what would happen if the makers of data analysis software like SPSS, SAS, etc. changed some of the defaults and options. Sort of in the spirit of Nudge — don’t necessarily change the list of what is ultimately possible to do, but make changes to make some things easier and other things harder (like via defaults and options).
Would people think about their data differently? Here’s my list of how I might change regression procedures, and what I think these changes might do:
1. Let users write common transformations of variables directly into the syntax. Things like centering, z-scoring, log-transforming, multiplying variables into interactions, etc. This is already part of some packages (it’s easy to do in R), but not others. In particular, running interactions in SPSS is a huge royal pain. For example, to do a simple 2-way interaction with centered variables, you have to write all this crap *and* cycle back and forth between the code and the output along the way:
desc x1 x2. * Run just the above, then look at the output and see what the means are, then edit the code below. compute x1_c = x1 - [whatever the mean was]. compute x2_c = x2 - [whatever the mean was]. compute x1x2 = x1_c*x2_c. regression /dependent y /enter x1_c x2_c x1x2.
Why shouldn’t we be able to do it all in one line like this?
regression /dependent y /enter center(x1) center(x2) center(x1)*center(x2).
The nudge: If it were easy to write everything into a single command, maybe more people would look at interactions more often. And maybe they’d stop doing median splits and then jamming everything into an ANOVA!
2. By default, the output shows you parameter estimates and confidence intervals.
3. Either by default or with an easy-to-implement option, you can get a variety of standardized effect size estimates with their confidence intervals. And let’s not make variance-explained metrics (like R^2 or eta^2) the defaults.
The nudge: #2 and #3 are both designed to focus people on point and interval estimation, rather than NHST.
This next one is a little more radical:
4. By default the output does not show you inferential t-tests and p-values — you have to ask for them through an option. And when you ask for them, you have to state what the null hypotheses are! So if you want to test the null that some parameter equals zero (as 99.9% of research in social science does), hey, go for it — but it has to be an active request, not a passive default. And if you want to test a null hypothesis that some parameter is some nonzero value, it would be easy to do that too.
The nudge. In the way a lot of statistics is taught in psychology, NHST is the main event and effect estimation is an afterthought. This would turn it around. And by making users specify a null hypothesis, it might spur us to pause and think about how and why we are doing so, rather than just mining for asterisks to put in tables. Heck, I bet some nontrivial number of psychology researchers don’t even know that the null hypothesis doesn’t have to be the nil hypothesis. (I still remember the “aha” feeling the first time I learned that you could do that — well along into graduate school, in an elective statistics class.) If we want researchers to move toward point or range predictions with strong hypothesis testing, we should make it easier to do.
All of these things are possible to do in most or all software packages. But as my SPSS example under #1 shows, they’re not necessarily easy to implement in a user-friendly way. Even R doesn’t do all of these things in the standard lm function. As a result, they probably don’t get done as much as they could or should.
Any other nudges you’d make?
Imagine that you have entered a charity drawing to win a free iPad. The charity organizer draws a ticket, and it’s your number. Hooray! But wait, someone else is cheering too. After a little investigation it turns out that due to a printing error, two different tickets had the same winning number. You don’t want to be a jerk and make the charity buy another iPad, and you can’t saw it in half. So you have to decide who gets the iPad.
Suppose that someone proposes to flip a coin to decide who gets the iPad. Sounds pretty fair, right?
But suppose that the other guy with a winning ticket — let’s call him Pete — instead proposes the following procedure. First the organizer will flip a coin. If Pete wins that flip, he gets the iPad. But if you win the flip, then the organizer will toss the coin 2 more times. If Pete wins best out of 3, he gets the iPad. If you win best out of 3, then the organizer will flip yet another 2 times. If Pete wins the best out of those (now) 5 flips, he gets the iPad. If not, keep going… Eventually, if Pete gets tired and gives up before he wins the iPad, you can have it.
Doesn’t sound so fair, does it?
The procedure I just described is not all that different from the research practice of data peeking. Data peeking goes something like this: you run some subjects, then do an analysis. If it comes out significant, you stop. If not, you run some more subjects and try again. What Peeky Pete’s iPad Procedure and data-peeking have in common is that you are starting with a process that includes randomness (coin flips, or the random error in subjects’ behavior) but then using a biased rule to stop the random process when it favors somebody’s outcome. Which means that the “randomness” is no longer random at all.
Statisticians have been studying the consequences of data-peeking for a long time (e.g., Armitage et al., 1969). But the practice has received new attention recently in psychology, in large part because of the Simmons et al. false-positive psychology paper that came out last year. Given this attention, it is fair to wonder (1) how common is data-peeking, and (2) how bad is it?
How common is data-peeking?
Anecdotally, lot of people seem to think data peeking is common. Tal Yarkoni described data peeking as “a time-honored tradition in the social sciences.” Dave Nussbaum wrote that “Most people don’t realize that looking at the data before collecting all of it is much of a problem,” and he says that until recently he was one of those people. Speaking from my own anecdotal experience, ever since Simmons et al. came out I’ve had enough casual conversations with colleagues in social psychology that have brought me around to thinking that data peeking is not rare. And in fact, I have talked to more than one fMRI researcher who considers data peeking not only acceptable but beneficial (more on that below).
More formally, when Leslie John and others surveyed academic research psychologists about questionable research practices, a majority (55%) outright admitted that they have “decid[ed] whether to collect more data after looking to see whether the results were significant.” John et al. use a variety of techniques to try to correct for underreporting; they estimate the real prevalence to be much higher. On the flip side, it is at least a little ambiguous whether some respondents might have interpreted “deciding whether to collect more data” to include running a new study, rather than adding new subjects to an existing one. But the bottom line is that data-peeking does not seem to be at all rare.
How bad is it?
You might be wondering, is all the fuss about data peeking just a bunch of rigid stats-nerd orthodoxy, or does it really matter? After all, statisticians sometimes get worked up about things that don’t make much difference in practice. If we’re talking about something that turns a 5% Type I error rate into 6%, is it really a big deal?
The short answer is yes, it’s a big deal. Once you start looking into the math behind data-peeking, it quickly becomes apparent that it has the potential to seriously distort results. Exactly how much depends on a lot of factors: how many cases you run before you take your first peek, how frequently you peek after that, how you decide when to keep running subjects and when to give up, etc. But a good and I think realistic illustration comes from some simulations that Tal Yarkoni posted a couple years ago. In one instance, Tal simulated what would happen if you run 10 subjects and then start peeking every 5 subjects after that. He found that you would effectively double your type I error rate by the time you hit 20 subjects. If you peek a little more intensively and run a few more subjects it gets a lot worse. Under what I think are pretty realistic conditions for a lot of psychology and neuroscience experiments, you could easily end up reporting p<.05 when the true false-positive rate is closer to p=20.
And that’s a serious difference. Most researchers would never dream of looking at a p=.19 in their SPSS output and then blatantly writing p<.05 in a manuscript. But if you data-peek enough, that could easily end up being de facto what you are doing, even if you didn’t realize it. As Tal put it, “It’s not the kind of thing you just brush off as needless pedantry.”
So what to do?
These issues are only becoming more timely, given current concerns about replicability in psychology. So what to do about it?
The standard advice to individual researchers is: don’t data-peek. Do a power analysis, set an a priori sample size, and then don’t look at your data until you are done for good. This should totally be the norm in the vast majority of psychology studies.
And to add some transparency and accountability, one of Psychological Science’s proposed disclosure statements would require you to state clearly how you determined your sample size. If that happens, other journals might follow after that. If you believe that most researchers want to be honest and just don’t realize how bad data-peeking is, that’s a pretty good way to spread the word. People will learn fast once their papers start getting sent back with a request to run a replication (or rejected outright).
But is abstinence the only way to go? Some researchers make a cost-benefit case for data peeking. The argument goes as follows: With very expensive procedures (like fMRI), it is wasteful to design high-powered studies if that means you end up running more subjects than you need to determine if there is an effect. (As a sidenote, high-powered studies are actually quite important if you are interested in unbiased (or at least less biased) effect size estimation, but that’s a separate conversation; here I’m assuming you only care about significance.) And on the flip side, the argument goes, Type II errors are wasteful too — if you follow a strict no-data-peeking policy, you might run 20 subjects and get p=.11 and then have to set aside the study and start over from scratch.
Of course, it’s also wasteful to report effects that don’t exist. And compounding that, studies that use expensive procedures are also less likely to get directly replicated, which means that false-positive errors are harder to get found out.
So if you don’t think you can abstain, the next-best thing is to use protection. For those looking to protect their p I have two words: interim analysis. It turns out this is a big issue in the design of clinical trials. Sometimes that is for very similar expense reasons. And sometimes it is because of ethical and safety issues: often in clinical trials you need ongoing monitoring so that you can stop the trial just as soon as you can definitively say that the treatment makes things better (so you can give it to the people in the placebo condition) or worse (so you can call off the trial). So statisticians have worked out a whole bunch of ways of designing and analyzing studies so that you can run interim analyses while keeping your false-positive rate in check. (Because of their history, such designs are sometimes called sequential clinical trials, but that shouldn’t chase you off — the statistics don’t care if you’re doing anything clinical.) SAS has a whole procedure for analyzing them, PROC SEQDESIGN. And R users have lots of options. (I don’t know if these procedures have been worked into fMRI analysis packages, but if they haven’t, they really should be.)
Very little that I’m saying is new. These issues have been known for decades. And in fact, the 2 recommendations I listed above — determine sample size in advance or properly account for interim testing in your analyses — are the same ones Tal made. So I could have saved some blog space and just said “please go read Armitage et al or Todd et al. or Yarkoni & Braver.” (UPDATE via a commenter: or Strube, 2006.)But blog space is cheap, and as far as I can tell word hasn’t gotten out very far. And with (now) readily available tools and growing concerns about replicability, it is time to put uncorrected data peeking to an end.
Pretty big news. Psychological Science is seriously discussing 3 new reform initiatives. They are outlined in a letter being circulated by Eric Eich, editor of the journal, and they come from a working group that includes top people from APS and several other scientists who have been active in working for reforms.
After reading it through (which I encourage everybody to do), here are my initial takes on the 3 initiatives:
Initiative 1: Create tutorials on power, effect size, and confidence intervals. There’s plenty of stuff out there already, but if PSci creates a good new source and funnels authors to it, it could be a good thing.
Initiative 2: Disclosure statements about research process (such as how sample size was determined, unreported measures, etc.) This could end up being a good thing, but it will be complicated. Simine Vazire, one of the working group members who is quoted in the proposal, puts it well:
We are essentially asking people to “incriminate” themselves — i.e., reveal information that, in the past, editors have treated as reasons not to publish a paper. If we want authors to be honest, I think they will want some explicit acknowledgement that some degree of messiness (e.g., a null result here and there) will be tolerated and perhaps even treated as evidence that the entire set of findings is even more plausible (a la [Gregory] Francis, [Uli] Schimmack, etc.).
I bet there would be low consensus about what kinds and amounts of messiness are okay, because no one is accustomed to seeing that kind of information on a large scale in other people’s studies. It is also the case that things that are problematic in one subfield may be more reasonable in another. And reviewers and editors who lack the time or local expertise to really judge messiness against merit may fall back on simplistic heuristics rather than thinking things through in a principled way. (Any psychologist who has ever tried to say anything about causation, however tentative and appropriately bounded, in data that was not from a randomized experiment probably knows what that feels like.)
Another basic issue is whether people will be uniformly honest in the disclosure statements. I’d like to believe so, but without a plan for real accountability I’m not sure. If some people can get away with fudging the truth, the honest ones will be at a disadvantage.
3. A special submission track for direct replications, with 2 dedicated Associate Editors and a system of pre-registration and prior review of protocols to allow publication decisions to be decoupled from outcomes. A replication section at a journal? If you’ve read my blog before you might guess that I like that idea a lot.
The section would be dedicated to studies previously published in Psychological Science, so in that sense it is in the same spirit as the Pottery Barn Rule. The pre-registration component sounds interesting — by putting a substantial amount of review in place before data are collected, it helps avoid the problem of replications getting suppressed because people don’t like the outcomes.
I feel mixed about another aspect of the proposal, limiting replications to “qualified” scientists. There does need to be some vetting, but my hope is that they will set the bar reasonably low. “This paradigm requires special technical knowledge” can too easily be cover for “only people who share our biases are allowed to study this effect.” My preference would be for a pro-data, pro-transparency philosophy. Make it easy for for lots of scientists to run and publish replication studies, and make sure the replication reports include information about the replicating researchers’ expertise and experience with the techniques, methods, etc. Then meta-analysts can code for the replicating lab’s expertise as a moderator variable, and actually test how much expertise matters.
My big-picture take. Retraction Watch just reported yesterday on a study showing that retractions, especially retractions due to misconduct, cause promising scientists to move to other fields and funding agencies to direct dollars elsewhere. Between alleged fraud cases like Stapel, Smeesters, and Sanna, and all the attention going to false-positive psychology and questionable research practices, psychology (and especially social psychology) is almost certainly at risk of a loss of talent and money.
Getting one of psychology’s top journals to make real reforms, with the institutional backing of APS, would go a long way to counteract those negative effects. A replication desk in particular would leapfrog psychology past what a lot of other scientific fields do. Huge credit goes to Eric Eich and everyone else at APS and the working group for trying to make real reforms happen. It stands a real chance of making our science better and improving our credibility.
This morning felt quite ignominious indeed, and naturally it reminded me of William James. From the Principles of Psychology, chapter 26, “Will”:
We know what it is to get out of bed on a freezing morning in a room without a fire, and how the very vital principle within us protests against the ordeal. Probably most persons have lain on certain mornings for an hour at a time unable to brace themselves to the resolve. We think how late we shall be, how the duties of the day will suffer; we say, “I must get up, this is ignominious,” etc.; but still the warm couch feels too delicious, the cold outside too cruel, and resolution faints away and postpones itself again and again just as it seemed on the verge of bursting the resistance and passing over into the decisive act. Now how do we ever get up under such circumstances? If I may generalize from my own experience, we more often than not get up without any struggle or decision at all. We suddenly find that we have got up. A fortunate lapse of consciousness occurs; we forget both the warmth and the cold; we fall into some revery connected with the day’s life, in the course of which the idea flashes across us, “Hollo! I must lie here no longer” – an idea which at that lucky instant awakens no contradictory or paralyzing suggestions, and consequently produces immediately its appropriate motor effects. It was our acute consciousness of both the warmth and the cold during the period of struggle, which paralyzed our activity then and kept our idea of rising in the condition of wish and not of will. The moment these inhibitory ideas ceased, the original idea exerted its effects.
James’s visible presence in contemporary psychology seem mostly limited to 2 roles. Someone finds a quote, puts it as an epigram at the top of their manuscript, and claims that their ideas have roots going more than a century back. Or alternatively someone finds a quote, puts it up as an epigram, and then claims that their ideas overturn more than a century of received wisdom.
But going back and actually re-reading James seriously is usually an enlightening activity. Just from that chapter on “Will” you can draw lines to contemporary research on delay of gratification, self-regulatory depletion, goal pursuit, the relationship between attention and executive control, and automaticity. James’s ideas about all of these topics are nuanced, with a lot of connections but few easy one-to-one mappings (whether supported or falsified) to contemporary research. Every once in a while I get the urge to go back and look at something James wrote, and if no contradictory or paralyzing suggestions stop me, I’m always glad that I did.
Every once in a while I get emails asking me about norms for the Big Five Inventory. I got one the other day, and I figured that if more than one person has asked about it, it’s probably worth a blog post.
There’s a way of thinking about norms — which I suspect is the most common way of thinking about norms — that treats them as some sort of absolute interpretive framework. The idea is that you could tell somebody, hey, if you got this score on the Agreeableness scale, it means you have this amount of agreeableness.
But I generally think that’s not the right way of thinking about it. Lew Goldberg put it this way:
One should be very wary of using canned “norms” because it isn’t obvious that one could ever find a population of which one’s present sample is a representative subset. Most “norms” are misleading, and therefore they should not be used.
That is because “norms” are always calculated in reference to some particular sample, drawn from some particular population (which BTW is pretty much never “the population of all human beings”). Norms are most emphatically NOT an absolute interpretation — they are unavoidably comparative.
So the problem arises because the usual way people talk about norms tends to bury that fact. So people say, oh, you scored at the 70th percentile. They don’t go on to say the 70th percentile of what. For published scales that give normed scores, it often turns out to mean the 70th percentile of the distribution of people who somehow made it into the scale author’s convenience sample 20 years ago.
So what should you do to help people interpret their scores? Lew’s advice is to use the sample you have at hand to construct local norms. For example, if you’re giving feedback to students in a class, tell them their percentile relative to the class.
Another approach is to use distributional information from existing dataset and just be explicit about what comparison you are making and where the data come from. For the BFI, I sometimes refer people to a large dataset of adult American Internet users that I used for a paper. Sample descriptives are in the paper, and we’ve put up a table of means and SDs broken down by age and gender for people who want to make those finer distinctions. You can then use those means and SDs to convert your raw scores into z-scores, and then calculate or look up the normal-distribution percentile. You would then say something like, “This is where you stand relative to a bunch of Internet users who took this questionnaire online.” (You don’t have to use that dataset, of course. Think about what would be an appropriate comparison group and then poke around Google Scholar looking for a paper that reports descriptive statistics for the kind of sample you want.)
Either the “local norms” approach or the “comparison sample” approach can work for many situations, though local norms may be difficult for very small samples. If the sample as a whole is unusual in some way, the local norms will remove the average “unusualness” whereas the comparison-sample approach will keep it in there, and you can decide which is the more useful comparison. (For example, an astronaut who scores in the 50th percentile of conscientiousness relative to other astronauts would be around the 93rd percentile relative to college undergrads.) But the most important thing is to avoid anything that sounds absolute. Be consistent and clear about the fact that you are making comparisons and about who you are comparing somebody to.
Let’s say that some theory states that people in psychological state A1 will engage in behavior B more than people in psychological state A2. Suppose that, a priori, the theory allows us to make this directional prediction, but not a prediction about the size of the effect.
A researcher designs an experiment — call this Study 1 — in which she manipulates A1 versus A2 and then measures B. Consistent with the theory, the result of Study 1 shows more of behavior B in condition A1 than A2. The effect size is d=0.8 (a large effect). A null hypothesis significance test shows that the effect is significantly different from zero, p<.05.
Now Researcher #2 comes along and conducts Study 2. The procedures of Study 2 copy Study 1 as closely as possible — the same manipulation of A, the same measure of B, etc. The result of Study 2 shows more of behavior B in condition A1 than in A2 — same direction as Study 1. In Study 2, the effect size is d=0.3 (a smallish effect). A null hypothesis significance test shows that the effect is significantly different from zero, p<.05. But a comparison of the Study 1 effect to the Study 2 effect (d=0.8 versus d=0.3) is also significant, p<.05.
Here’s the question: did Study 2 successfully replicate Study 1?
My answer is no. Here’s why. When we say “replication,” we should be talking about whether we can reproduce a result. A statistical comparison of Studies 1 and 2 shows that they gave us significantly different results. We should be bothered by the difference, and we should be trying to figure out why.
People who would call Study 2 a “successful” replication of Study 1 are focused on what it means for the theory. The theoretical statement that inspired the first study only spoke about direction, and both results came out in the same direction. By that standard you could say that it replicated.
But I have two problems with defining replication in that way. My first problem is that, after learning the results of Study 1, we had grounds to refine the theory to include statements about the likely range of the effect’s size, not just its direction. Those refinements might be provisional, and they might be contingent on particular conditions (i.e., the experimental conditions under which Study 1 was conducted), but we can and should still make them. So Study 2 should have had a different hypothesis, a more focused one, than Study 1. Theories should be living things, changing every time they encounter new data. If we define replication as testing the theory twice then there can be no replication, because the theory is always changing.
My second problem is that we should always be putting theoretical statements to multiple tests. That should be such normal behavior in science that we shouldn’t dilute the term “replication” by including every possible way of doing it. As Michael Shermer once wrote, “Proof is derived through a convergence of evidence from numerous lines of inquiry — multiple, independent inductions all of which point to an unmistakable conclusion.” We should all be working toward that goal all the time.
This distinction — between empirical results vs. conclusions about theories — goes to the heart of the discussion about direct and conceptual replication. Direct replication means that you reproduce, as faithfully as possible, the procedures and conditions of the original study. So the focus should rightly be on the result. If you get a different result, it either means that despite your best efforts something important differed between the two studies, or that one of the results was an accident.
By contrast, when people say “conceptual replication” they mean that they have deliberately changed one or more major parts of the study — like different methods, different populations, etc. Theories are abstractions, and in a “conceptual replication” you are testing whether the abstract theoretical statement (in this case, B|A1 > B|A2) is still true under a novel concrete realization of the theory. That is important scientific work, but it differs in huge, qualitative ways from true replication. As I’ve said, it’s not just a difference in empirical procedures; it’s a difference in what kind of inferences you are trying to draw (inferences about a result vs. inferences about a theoretical statement). Describing those simply as 2 varieties of the same thing (2 kinds of replication) blurs this important distinction.
I think this means a few important things for how we think about replications:
1. When judging a replication study, the correct comparison is between the original result and the new one. Even if the original study ran a significance test against a null hypothesis of zero effect, that isn’t the test that matters for the replication. There are probably many ways of making this comparison, but within the NHST framework that is familiar to most psychologists, the proper “null hypothesis” to test against is the one that states that the two studies produced the same result.
2. When we observe a difference between a replication and an original study, we should treat that difference as a problem to be solved. Not (yet) as a conclusive statement about the validity of either study. Study 2 didn’t “fail to replicate” Study 1; rather, Studies 1 and 2 produced different results when they should have produced the same, and we now need to figure out what caused that difference.
3. “Conceptual replication” should depend on a foundation of true (“direct”) replicability, not substitute for it. The logic for this is very much like how validity is strengthened by reliability. It doesn’t inspire much confidence in a theory to say that it is supported by multiple lines of evidence if all of those lines, on their own, give results of poor or unknown consistency.