Everything is fucked: The syllabus

PSY 607: Everything is Fucked
Prof. Sanjay Srivastava
Class meetings: Mondays 9:00 – 10:50 in 257 Straub
Office hours: Held on Twitter at your convenience (@hardsci)

In a much-discussed article at Slate, social psychologist Michael Inzlicht told a reporter, “Meta-analyses are fucked” (Engber, 2016). What does it mean, in science, for something to be fucked? Fucked needs to mean more than that something is complicated or must be undertaken with thought and care, as that would be trivially true of everything in science. In this class we will go a step further and say that something is fucked if it presents hard conceptual challenges to which implementable, real-world solutions for working scientists are either not available or routinely ignored in practice.

The format of this seminar is as follows: Each week we will read and discuss 1-2 papers that raise the question of whether something is fucked. Our focus will be on things that may be fucked in research methods, scientific practice, and philosophy of science. The potential fuckedness of specific theories, research topics, etc. will not be the focus of this class per se, but rather will be used to illustrate these important topics. To that end, each week a different student will be assigned to find a paper that illustrates the fuckedness (or lack thereof) of that week’s topic, and give a 15-minute presentation about whether it is indeed fucked.


20% Attendance and participation
30% In-class presentation
50% Final exam

Week 1: Psychology is fucked

Meehl, P. E. (1990). Why summaries of research on psychological theories are often uninterpretable. Psychological Reports, 66, 195-244.

Week 2: Significance testing is fucked

Cohen, J. (1990). Things I have learned (so far). American Psychologist, 45, 1304-1312.

Rouder, J. N., Morey, R. D., Verhagen, J., Province, J. M., & Wagenmakers, E. J. (2016). Is there a free lunch in inference? Topics in Cognitive Science, 8, 520-547.

Week 3: Causal inference from experiments is fucked

Chapter 3 from: Bollen, K. A. (1989). Structural equations with latent variables. New York: Wiley.

Week 4: Mediation is fucked

Bullock, J. G., Green, D. P., & Ha, S. E. (2010). Yes, but what’s the mechanism?(don’t expect an easy answer). Journal of Personality and Social Psychology, 98, 550-558.

Week 5: Covariates are fucked

Culpepper, S. A., & Aguinis, H. (2011). Using analysis of covariance (ANCOVA) with fallible covariates. Psychological Methods, 16, 166-178.

Westfall, J., & Yarkoni, T. (2016). Statistically controlling for confounding constructs is harder than you think. PloS one, 11, e0152719.

Week 6: Replicability is fucked

Pashler, H., & Harris, C. R. (2012). Is the replicability crisis overblown? Three arguments examined. Perspectives on Psychological Science, 7, 531-536.

Open Science Collaboration. (2015). Estimating the reproducibility of psychological science. Science, 349(6251), aac4716.

Week 7: Interlude: Everything is fine, calm the fuck down

Gilbert, D. T., King, G., Pettigrew, S., & Wilson, T. D. (2016). Comment on “Estimating the reproducibility of psychological science.” Science, 251, 1037a.

Maxwell, S. E., Lau, M. Y., & Howard, G. S. (2015). Is psychology suffering from a replication crisis? What does “failure to replicate” really mean? American Psychologist, 70, 487-498.

Week 8: Scientific publishing is fucked

Fanelli, D. (2011). Negative results are disappearing from most disciplines and countries. Scientometrics, 90, 891-904.

Ioannidis, J. P. (2005). Why most published research findings are false. PLoS Med, 2, e124.

Week 9: Meta-analysis is fucked

Inzlicht, M., Gervais, W., & Berkman, E. (2015). Bias-Correction Techniques Alone Cannot Determine Whether Ego Depletion is Different from Zero: Commentary on Carter, Kofler, Forster, & McCullough, 2015. Available at SSRN: http://ssrn.com/abstract=2659409 or http://dx.doi.org/10.2139/ssrn.2659409

Van Elk, M., Matzke, D., Gronau, Q. F., Guan, M., Vandekerckhove, J., & Wagenmakers, E. J. (2015). Meta-analyses are no substitute for registered replications: A skeptical perspective on religious priming. Frontiers in Psychology, 6.

Week 10: The scientific profession is fucked

Bakker, M., van Dijk, A., & Wicherts, J. M. (2012). The rules of the game called psychological science. Perspectives on Psychological Science, 7, 543-554.

Nosek, B. A., Spies, J. R., & Motyl, M. (2012). Scientific utopia II. Restructuring incentives and practices to promote truth over publishability. Perspectives on Psychological Science, 7, 615-631.

Finals week

Wear black and bring a #2 pencil.

An eye-popping ethnography of three infant cognition labs

I don’t know how else to put it. David Peterson, a sociologist, recently published an ethnographic study of 3 infant cognition labs. Titled “The Baby Factory: Difficult Research Objects, Disciplinary Standards, and the Production of Statistical Significance,” it recounts his time spend as a participant observer in those labs, attending lab meetings and running subjects.

In his own words, Peterson “shows how psychologists produce statistically significant results under challenging circumstances by using strategies that enable them to bridge the distance between an uncontrollable research object and a professional culture that prizes methodological rigor.” The account of how the labs try to “bridge the distance” reveals one problematic practice after another, in a way that sometimes makes them seem like normal practice and no big deal to the people in the labs. Here are a few examples.

Protocol violations that break blinding and independence:

…As a routine part of the experiments, parents are asked to close their eyes to prevent any unconscious influence on their children. Although this was explicitly stated in the instructions given to parents, during the actual experiment, it was often overlooked; the parents’ eyes would remain open. Moreover, on several occasions, experimenters downplayed the importance of having one’s eyes closed. One psychologist told a mother, “During the trial, we ask you to close your eyes. That’s just for the journals so we can say you weren’t directing her attention. But you can peek if you want to. It’s not a big deal. But there’s not much to see.”

Optional stopping based on data peeking:

Rather than waiting for the results from a set number of infants, experimenters began “eyeballing” the data as soon as babies were run and often began looking for statistical significance after just 5 or 10 subjects. During lab meetings and one-on-one discussions, experiments that were “in progress” and still collecting data were evaluated on the basis of these early results. When the preliminary data looked good, the test continued. When they showed ambiguous but significant results, the test usually continued. But when, after just a few subjects, no significance was found, the original protocol was abandoned and new variations were developed.

Invalid comparisons of significant to nonsignificant:

Because experiments on infant subjects are very costly in terms of both time and money, throwing away data is highly undesirable. Instead, when faced with a struggling experiment using a trusted experimental paradigm, experimenters would regularly run another study that had higher odds of success. This was accomplished by varying one aspect of the experiment, such as the age of the participants. For instance, when one experiment with 14-month-olds failed, the experimenter reran the same study with 18-month-olds, which then succeeded. Once a significant result was achieved, the failures were no longer valueless. They now represented a part of a larger story: “Eighteen-month-olds can achieve behavior X, but 14-month-olds cannot.” Thus, the failed experiment becomes a boundary for the phenomenon.

And HARKing:

When a clear and interesting story could be told about significant findings, the original motivation was often abandoned. I attended a meeting between a graduate student and her mentor at which they were trying to decipher some results the student had just received. Their meaning was not at all clear, and the graduate student complained that she was having trouble remembering the motivation for the study in the first place. Her mentor responded, “You don’t have to reconstruct your logic. You have the results now. If you can come up with an interpretation that works, that will motivate the hypothesis.”

A blunt explanation of this strategy was given to me by an advanced graduate student: “You want to know how it works? We have a bunch of half-baked ideas. We run a bunch of experiments. Whatever data we get, we pretend that’s what we were looking for.” Rather than stay with the original, motivating hypothesis, researchers in developmental science learn to adjust to statistical significance. They then “fill out” the rest of the paper around this necessary core of psychological research.

Peterson discusses all this in light of recent discussions about replicability and scientific practices in psychology. He says that researchers have basically 3 choices: limit the scope of your questions to what you can do well with available methods, relax our expectations of what a rigorous study looks like, or engage in QRPs. I think that is basically right. It is why I believe that any attempt to reduce QRPs has to be accompanied by changes to incentive structures, which govern the first two.

Peterson also suggests that QRPs are “becoming increasingly unacceptable.” That may be true in public discourse, but the inside view presented by his ethnography suggests that unless more open practices become standard, labs will continue to have lots of opportunity to engage in them and little incentive not to.

UPDATE: I discuss what all this means in a followup post: Reading “The Baby Factory” in context.

Failed experiments do not always fail toward the null

There is a common argument among psychologists that null results are uninformative. Part of this is the logic of NHST – failure to reject the null is not the same as confirmation of the null. Which is an internally valid statement, but ignores the fact that studies with good power also have good precision to estimate effects.

However there is a second line of argument which is more procedural. The argument is that a null result can happen when an experimenter makes a mistake in either the design or execution of a study. I have heard this many times; this argument is central to an essay that Jason Mitchell recently posted arguing that null replications have no evidentiary value. (The essay said other things too, and has generated some discussion online; see e.g., Chris Said’s response.)

The problem with this argument is that experimental errors (in both design and execution) can produce all kinds of results, not just the null. Confounds, artifacts, failures of blinding procedures, demand characteristics, outliers and other violations of statistical assumptions, etc. can all produce non-null effects in data. When it comes to experimenter error, there is nothing special about the null.

Moreover, we commit a serious oversight when we use substantive results as the sole evidence of procedures. Say that the scientific hypothesis is that X causes Y. So we design an experiment with an operationalization of X, O_X, and an operationalization of Y, O_Y. A “positive” result tells us O_X -> O_Y. But unless we can say something about the relationships between O_X and X and between O_Y and Y, the result tells us nothing about X and Y.

We have a well established framework for doing that with measurements: construct validation. We expect that measures can and should be validated independent of results to document that Y -> O_Y (convergent validity) and P, Q, R, etc. !-> O_Y (discriminant validity). We have papers showing that measurement procedures are generally valid (in fact these are some of our most-cited papers!). And we typically expect papers that apply previously-established measurement procedures to show that the procedure worked in a particular sample, e.g. by reporting reliability, factor structure, correlations with other measures, etc.

Although we do not seem to publish as many validation papers on experimental manipulations as on measurements, the logic of validation applies just as well. We can obtain evidence that O_X -> X, for example by showing that experimental O_X affects already-established measurements O_X2, O_X3, etc. And in a sufficiently powered design we can show that O_X does not meaningfully influence other variables that are known to affect Y or O_Y. Just as with measurements, we can accumulate this evidence in systematic investigations to show that procedures are generally effective, and then when labs use the procedures to test substantive hypotheses they can run manipulation checks to show that they are executing a procedure correctly.

Programmatic validation is not always necessary — some experimental procedures are so face-valid that we are willing to accept that O_X -> X without a validation study. Likewise for some measurements. That is totally fine, as long as there is no double standard. But in situations where we would be willing to question whether a null result is informative, we should also be willing to question whether a non-null is. We need to evaluate methods in ways that do not depend on whether those methods give us results we like — for experimental manipulations and measurements alike.

An editorial board discusses fMRI analysis and “false-positive psychology”

Update 1/3/2012: I have seen a few incoming links describing the Psych Science email discussion as “leaked” or “made public.” For the record, the discussion was forwarded to me from someone who got it from a professional listserv, so it was already out in the open and circulating before I posted it here. Considering that it was carefully redacted and compiled for circulation by the incoming editor-in-chief, I don’t think “leaked” is a correct term at all (and “made public” happened before I got it).


I recently got my hands on an email discussion among the Psychological Science editorial board. The discussion is about whether or how to implement recommendations by Poldrack et al. (2008) and Simmons, Nelson, and Simonsohn (2011) for research methods and reporting. The discussion is well worth reading and appears to be in circulation already, so I am posting it here for a wider audience. (All names except the senior editor, John Jonides, and Eric Eich who compiled the discussion, were redacted by Eich; commenters are instead numbered.)

The Poldrack paper proposes guidelines for reporting fMRI experiments. The Simmons paper is the much-discussed “false-positive psychology” paper that was itself published in Psych Science. The argument in the latter is that slippery research and reporting practices can produce “researcher degrees of freedom” that inflate Type I error. To reduce these errors, they make 6 recommendations for researchers and 4 recommendations for journals to reduce these problems.

There are a lot of interesting things to come out of the discussion. Regarding the Poldrack paper, the discussion apparently got started when a student of Jonides analyzed the same fMRI dataset under several different defensible methods and assumptions and got totally different results. I can believe that — not because I have extensive experience with fMRI analysis (or any hands-on experience at all), but because that’s true with any statistical analysis where there is not strong and widespread consensus on how to do things. (See covariate adjustment versus difference scores.)

The other thing about the Poldrack discussion that caught my attention was commenter #8, who asked that more attention be given to selection and determination of ROIs. S/he wrote:

We, as psychologists, are not primarily interested in exploring the brain. Rather, we want to harness fMRI to reach a better understanding of psychological process. Thus, the choice of the various ROIs should be derived from psychological models (or at least from models that are closely related to psychological mechanisms). Such a justification might be an important editorial criterion for fMRI studies submitted to a psychological journal. Such a psychological model might also include ROIs where NO activity is expected, control regions, so to speak.

A.k.a. convergent and discriminant validity. (Once again, the psychometricians were there first.) A lot of research that is billed (in the press or in the scientific reports themselves) as reaching new conclusions about the human mind is really, when you look closely, using established psychological theories and methods as a framework to explore the brain. Which is a fine thing to do, and in fact is a necessary precursor to research that goes the other way, but shouldn’t be misrepresented.

Turning to the Simmons et al. piece, there was a lot of consensus that it had some good ideas but went too far, which is similar to what I thought when I first read the paper. Some of the Simmons recommendations were so obviously important that I wondered why they needed to be made at all, because doesn’t everybody know them already? (E.g., running analyses while you collect data and using p-values as a stopping rule for sample size — a definite no-no.) The fact that Simmons et al. thought this needed to be said makes me worried about the rigor of the average research paper. Other of their recommendations seemed rather rigid and targeted toward a pretty small subset of research designs. The n>20 rule and the “report all your measures” rule might make sense for small-and-fast randomized experiments of the type the authors probably mostly do themselves, but may not work for everything (case studies, intensive repeated-measures studies, large multivariate surveys and longitudinal studies, etc.).

Commenter #8 (again) had something interesting to say about a priori predictions:

It is always the educated reader who needs to be persuaded using convincing methodology. Therefore, I am not interested in the autobiography of the researcher. That is, I do not care whether s/he has actually held the tested hypothesis before learning about the outcomes…

Again, an interesting point. When there is not a strong enough theory that different experts in that theory would have drawn the same hypotheses independently, maybe a priori doesn’t mean much? Or put a little differently: a priori should be grounded in a publicly held and shared understanding of a theory, not in the contents of an individual mind.

Finally, a general point that many people made was that Psych Science (and for that matter, any journal nowadays) should make more use of supplemental online materials (SOM). Why shouldn’t stimuli, scripts, measures, etc. — which are necessary to conduct exact replications — be posted online for every paper? In current practice, if you want to replicate part or all of someone’s procedure, you need to email the author. Reviewers almost never have access to this material, which means they cannot evaluate it easily. I have had the experience of getting stimuli or measures for a published study and seeing stuff that made me worry about demand characteristics, content validity, etc. That has made me wonder why reviewers are not given the opportunity to closely review such crucial materials as a matter of course.

Oh, that explains it

A new study by Timothy Salthouse adds to the body of work suggesting that raw cognitive performance begins to decline in early adulthood.

News reports are presenting the basic age pattern as a new finding. It’s not, or at least it’s not new in the way it’s being portrayed. The idea that fluid intelligence peaks in the 20s and then declines has been around for a while. I remember learning it as an undergrad. I teach it in my Intro classes.

So why is a new study being published? Because the research, reported in Neurobiology of Aging, tries to tease apart some thorny methodological problems in estimating how mental abilities change with age.

If you simply compare different people of different ages (a cross-sectional design), you don’t know if the differences are because of what happens to people as they get older, or instead because of cohort effects (i.e., generational differences). In other words, maybe members of more recent generations do better at these tasks by virtue of better schooling, better early nutrition, or something like that. In that case, apparent differences between old people and young people might have nothing to do with the process of getting older per se.

To avoid cohort effects, you could follow the same people over time (a longitudinal design). However, if you do that you have to worry about something else — practice effects. The broad underlying ability may be declining, but people might be getting “test-smart” if you give them the same (or similar) tests again and again, which would mask any true underlying decline.

As a result of different findings obtained with different methods, there was a majority view among researchers that fluid performance starts to decline in early adulthood, but also a significant minority view that that declines happen later.

What Salthouse did was to look at cross-sectional and longitudinal data side-by-side in a way that allowed him to estimate the age trajectory after accounting for both kinds of biases. In principle, this should yield more precise estimates than previous studies about the particular shape of the trend. Based on the combined data, Salthouse concluded that the early-adulthood peak was more consistent with the evidence.

It’s understandable, but unfortunate, that the media coverage isn’t going into this level of nuance. Science is incremental, and this study is a significant contribution (though by no means the last word). But news stories often have a set narrative – the lone scientist having a “eureka!” moment with a shattering breakthrough that “proves” his theory. Science doesn’t work that way, but that’s the way it’s usually covered.