The ACE Article and Those Confounded Effect Sizes

There is a kind of psychology research article I have seen many times over the past 20 years. My pet name for it is the “ACE” because it goes like this:

  • Archival
  • Correlational
  • Experimental

These three phases, in that order, each with one or more studies. To invent an example, imagine we’re testing whether swearing makes you more likely to throw things … via a minimal ACE article.

(To my knowledge, there is no published work on this topic, but mea culpa if this idea is your secret baby.)

First, give me an “A” — Archival! We choose to dig up the archives of the US Tennis Association, covering all major matches from 1999 to 2007. Lucky for us, they have kept records of unsporting incidents for each player at each match, including swearing and throwing the racket. Using multilevel statistics, we find that indeed, the more a player curses in a match, the more they throw the racket. The effect size is a healthy r = .50, p  < .001.

Now, give me a “C” — Correlational! We give 300 online workers a questionnaire, where we ask how often they have cursed in the last 7 days, and how often they have thrown something in anger in the same time period. The two measures are correlated r = .17, p = .003.

Finally, give me an “E” — Experimental! We bring 100 undergraduates into the lab. We get half of them to swear profusely for one full minute, the other half to rattle off as many names of fish as they can think of. We then let them throw squash balls against a target electronically emblazoned with the face of their most hated person, a high-tech update of the dart task in Rozin, Millman and Nemeroff (1986). And behold, the balls fly faster and harder in the post-swearing condition than in the post-fish condition, t(98) = 2.20, d=0.44, p = .03.

Aesthetically, this model is pleasing. It embraces a variety of settings and populations, from the most naturalistic (tennis) to the most constrained (the lab). It progresses by eliminating confounds. We start with two settings, the Archival and Correlational, where throwing and cursing stand in an uncertain relation to each other. Their association, after all, could just be a matter of causation going either way, or third variables causing both. The Experiment makes it clearer. The whole package presents a compelling, full-spectrum accumulation of proof for the hypothesis. After all, the results are all significant, right?

But in the new statistical era, we care about more than just the significance of individual studies. We care about effect size across the studies. Effect size helps us integrate the evidence from non-significant studies and significant ones, under standards of full reporting. It goes into meta-analyses, both within the article and on a larger scale. It lets us calculate the power of the studies, informing analyses of robustness such as p-curve and R-index.

Effect sizes, however, are critically determined by the methods used to generate them.  I would bet that many psychologists think about effect size as some kind of Platonic form, a relationship between variables in the abstract state. But effect size cannot be had except through research methods. And methods can:

  • give the appearance of a stronger effect than warranted, through confounding variables;
  • or obscure an effect that actually exists, through imprecision and low power.

So, it’s complicated to extract a summary effect size from the parts of an ACE. The archival part, and to some extent the correlational, will have lots of confounding. More confounds may remain even after controlling for the obvious covariates. Experimental data may suffer from measurement noise, especially if subtle or field methods are used.

And, indeed, all parts might yield an inflated estimate if results and analyses are chosen selectively. The archival part is particularly prone to suspicions of post-hoc peeking. Why those years and not other ones? Why thrown tennis rackets and not thrown hockey sticks? Why Larry the lawyer and Denise the dentist, but not Donna the doctor or Robbie the rabbi (questions asked of research into the name-letter effect; Gallucci, 2003, pdf)? Pre-registration of these decisions, far from being useless for giving confidence in archival studies, almost seems like a requirement, provided it happens before the data are looked at in depth.

The ACE’s appeal requires studies with quite different methods. When trying to subject it to p-curves, mini-meta-analyses (Goh, Hall & Rosenthal, 2016; pdf), or other aggregate “new statistics,” we throw apples and oranges in the blender together. If evidence from the experiment is free from confounds but statistically weak, and the evidence from the archival study is statistically strong and big but full of confounds, does the set of studies really show both strong and unconfounded evidence?



The 18th century showman Wolfgang von Kempelen had a way to convince spectators there was no human agent inside his chess-playing “automaton”. He would open first one cabinet, then the other, while the human player inside moved his torso into the concealed parts. At no time was the automaton (yes, the famous “Mechanical Turk“)  fully open for view. Likewise, the ACE often has no study that combines rigorous method with robust finding. So, it’s hard to know what conclusions we should draw about effect size and significance on an article-wise level.

Leif Nelson at the Data Colada blog has recently taken a pessimistic view on finding the true effect size behind any research question. As he argues, the effect size has to take into account all possible studies that could have been run. So, evidence about it will always be incomplete.

Still, I think a resolution is possible, if we understand the importance of method. Yes, the best effect size takes into account both underlying effect and method used. But not all methods are equal. To have the clearest view of an underlying effect, we should focus on those methods that best meet the two criteria above: the least confounded with other factors, while at the same time being the most precise, sensitive, and free from error.

I said “possible,” not “easy.” For the first criterion, we need some agreement about which factors are confounds, and which are part of the effect.  For example, we show that science knowledge correlates with a “liberal”-“conservative” political self-report item. Then, trying to eliminate confounds, we covary out religious fundamentalism, right-wing authoritarianism, and support for big government. The residual of the lib-con item now represents a strange “liberal” who by statistical decree is just as likely as an equally strange “conservative” to be an anti-government authoritarian fundamentalist. In trying to purify a concept, you can end up washing it clean away.

Experimental methods make it somewhat easier to isolate an effect, but even then controversy might swirl around whether the effect has been whittled down to something too trivial or ecologically invalid to matter. A clear definition of the effect is also necessary in experiments. For example, whether you see implicit manipulations as the ultimate test of an effect depends on how much you see participant awareness and demand as part of the effects, or part of the problem. And are we content to look at self-reports of mental phenomena, or do we demand a demonstration of (messier? noisier?) behavioral effects as well? Finally, the effect size is going to be larger if you are only interested in the strength of an intervention versus no intervention — in which case, bring on the placebo effect, if it helps! It will usually be smaller, though, if you are interested in theoretically nailing down the “active ingredient” in that intervention.

The second criterion of precision is better studied. Psychometricians already know a lot about reducing noise in studies through psychometric validation. Indeed, there is a growing awareness that the low reliability and validity of many measures and manipulations in psychological research is a problem (Flake, Pek & Hehman, 2017, pdf). Even if the process of testing methods for maximum reliability is likely to be tedious, it is, theoretically, within our grasp.

But in a final twist, these two criteria often work against each other in research. Trying to reach good statistical power, it is harder to run large numbers of participants in controlled lab experiments than in questionnaire or archival data collections. Trying to avoid participant awareness confounds, implicit measures often increase measurement “noise” (Gawronski & De Houwer, 2014; Krause et al., 2011). This means it will be hard to get agreement about what method simultaneously maximizes the clarity of the effect  and its construct validity. But the alternative is pessimism about the meaning of the effect size, and a return to direction-only statistics.

I’ll conclude, boldly. It is meaningless to talk about the aggregate effect size in an ACE-model article, or to apply any kind of aggregate test to it that depends on effect sizes, such as p-curve. The results will depend, arbitrarily, on how many studies are included using each kind of method. A litmus test: would these studies all be eligible for inclusion in a single quantative meta-analysis? Best practice in meta-analysis demands that we define carefully the design of studies for inclusion, so that they are comparable with each other. Knowing what we know about methodology and effect size, the article, like the meta-analysis, is only a valid unit of aggregation if its studies’ methods are comparable with each other. The ACE article presents a compelling variety of methods and approaches, but that very quality is its Achilles’ heel when it comes to the “new statistics.”


Powering Your Interaction

With all the manuscripts I see, as editor-in-chief of Journal of Experimental Social Psychology, it’s clear that authors are following a wide variety of standards for statistical power analysis. In particular, the standards for power analysis of interaction effects are not clear. Most authors simply open up GPower software and plug in the numerator degrees of freedom of the interaction effect, which gives a very generous estimate.

I often hear that power analysis is impossible to carry out for a novel effect, because you don’t know the effect size ahead of time. But for novel effects that are built upon existing ones, a little reasoning can let you guess the likely size of the new one. That’s the good news. The bad news is: you’re usually going to need a much bigger sample to get decent power than GPower alone will suggest.

Heather’s Trilemma

Image result for music fast forward

Meet our example social psychologist, Heather. In an Experiment 1, she has participants listen either to a speeded-up or normal-tempo piece of mildly pleasant music. Then they fill out a mood questionnaire.  She wants to give her experiment 80% power to detect a medium effect, d = .5. Using GPower software, for a between-subjects t-test, this requires n = 64 in each condition, or N = 128 total.

The result actually shows a slightly larger effect size, d = .63. People are significantly happier after listening to the speeded-up music. Heather now wants to expand into a 2 x 2 between-subjects design that tests the effect’s moderation by the intensity of the music. So, she crosses the tempo manipulation with whether the music is mildly pleasant or intensely pleasant.

But there are three different authorities out there for this power analysis. And each is telling Heather different things.

  1. Heather assumes that the interaction effect is not known, even if the main effect is, so she goes with a medium effect again, d = .5. Using GPower, she tests the N needed to achieve 80% power of an interaction in this 2 x 2 ANOVA design, with 1 degree of freedom and f = .25 (that is, d = .5). GPower tells her that again, she needs only a total of 128, but now divided among 4 cells, for 32 people per cell. Because this power test of the interaction uses the same numerator df and other inputs as for the main effect, it gives the same result for N.
  2. Heather, however, always heard in graduate school that you should base factorial designs on a certain n per cell. Your overall N should grow, not stay the same, as the design gets more complex. In days of old, the conventional wisdom said n=20 was just fine. Now, the power analysis of the first experiment shows that you need over three times that number. Still, n=64 per cell should mean that you need N=256 people in the 2 x 2 experiment, not 128, right? What’s the real story?
  3. Then, Heather runs across a Data Colada blog post from a few years ago, “No-Way Interactions” by Uri Simonsohn. It said you actually need to quadruple, not just double, your overall N in order to move from a main effect design to a between-subjects interaction design. So Heather’s Experiment 2 would require 512 participants, not 256!

Most researchers at the time just shrugged at the Colada revelations (#3), said something like “We’re doomed” or “I tried to follow the math but it’s hard” or “These statistical maniacs are making it impossible to do psychology,” and went about their business. I can say with confidence that not a single one out of over 800 manuscripts I have triaged at JESP has cited the “No-Way” reason to use higher cell n when testing an interaction than a main effect!

But guess what? For most analyses in social psychology, answer #3 is the correct one. The “No-Way” argument deserves to be understood better. First, you need to know that the test of the interaction, by itself, is usually not adequate as a full model of the hypotheses you have. Second, you need to know how to estimate the expected effect size of an interaction when all you have is a prior main effect.

Power of a Factorial Analysis: Not so Simple

Answer #1, above (from basic power analysis) forgets that we are usually not happy just to see a significant interaction. No, we want to show more, that the interaction corresponds to a pattern of means that supports our conclusion. Here is an example showing that the shape of the interaction does matter, when you add in different configurations of main effects.


Result A shows the interaction you would get if Heather’s new experiment replicates the effect of tempo found in the old experiment when the music is mildly pleasant. For intensely pleasant music, there is no effect of tempo — a boundary condition limiting the original effect! The interaction coexists with a main effect of tempo, where faster music leads to better mood overall. Let’s say this was Heather’s hypothesis all along: the effect will replicate, but is “knocked out” if the music is too intense.

Result B also shows an interaction, with the same difference between slopes, and thus the same significance level and effect size. Intense is “less positive” than mild. But now the interaction is coexisting with two different main effects. Faster music worsens mood, and intense music improves it. Here, the mild version shows no effect of tempo on mood, and the intense version actually reduces mood with the fast vs. normal tempo. This doesn’t seem like such a good fit to the hypothesis!

Because these outcomes of the same interaction effect look so different, you need simple effects tests in order to fully test the stated hypotheses.  And yes, most authors know this, and duly present simple tests breaking down their interaction. But this means that answer #2 (n calculated per-cell) is more correct than answer #1 (N calculated by the interaction test). The more cells, the more overall N you need to adequately power the smallest-scale simple test.

Extending the Effect Size in a Factorial Analysis

That’s one issue. The other issue is how you can guess at the size of the interaction when you add another condition. This is not impossible. It can be estimated from the size of the original effect that you’re building the interaction upon, if you have an idea what the shape of the interaction is going to be.

Let’s start by asking when the interaction’s effect size is likely to be about the same as the original main effect size. Here I’m running a couple of analyses with example data and symmetrical means. If the new condition’s effect (orange dots) is the same size as the existing effect but in the other direction — a “reversal” effect — that’s when the interaction effect size, converted to d, is approximately the same as the original effect size. A power analysis of the interaction alone suggests you need about half as many participants per cell (n = 19!). That’s Heather’s answer #1. But, a power analysis of each of the simple effects — each as big as the original effect — suggests that you need about the same number per cell (n = 38), or twice as many in total. We’ve already established that the simple effects are the power analyses to focus on, and so it looks like Heather’s answer #2 is right in this case.

N(80) is the total sample to get 80% power, likewise for the interaction and simple effects.

Unfortunately, very few times in psychology do we add a factor and expect a complete reversal of the effect. For example, maybe you found that competent fellow team members in a competition are seen in a better light than incompetent ones. You add a condition where you evaluate members of the opposing team. Then you would expect that the incompetent ones would be more welcome, and the competent ones less so. That is the kind of situation you need in order to see a complete reversal.

However, it’s more usual that we expect the new condition to alter the size, rather than direction, of the existing effect. In the strongest such case, a new condition “knocks out” the old effect. Perhaps you found that men get more angry in a frustrating situation than women. Then you add a baseline condition (orange dots), a calm situation where you’d expect no gender differences in anger. The example shown below,  to the left, reveals that the interaction effect size here will be about half that of the original, strong gender effect. So, you need more power: roughly four times the number suggested by the mere GPower analysis of the interaction effect. This is Simonsohn’s recommendation too in the “knockout” case. But you can’t derive it using GPower, without realizing that your estimate of the interaction’s size has to be smaller than its constituent simple effect.

Again, the Ns to get 80% power for the interaction and for the largest simple effect are shown.

Even more typically, we might expect the new condition to attenuate but not completely knock out the effect. What if, even in a resting state, men express more anger than women? Let’s say that resting-state gender differences are about half the size of that shown when in a frustrated state. This is the example on the right, above.

It’s an interaction pattern that is not uncommon to see in published research. But it also has a very small interaction effect size, about 1/4 that of the simple effect in the “frustrated” state. As a result, the full design takes over 1,000 participants to achieve adequate power for the interaction.

I often see reports where a predicted simple effects test is significant but the overall interaction is not. The examples show why: in all but reversal effects, the simple effects tests require fewer people to get decent power than the interaction effects tests do. But the interaction is important, too. It is the test of differences among simple effects. If your hypothesis is merely satisfied by one simple effect being significant and another one not, you are committing the error of mistaking a “difference in significance” for a “significant difference.”

To sum up, the dire pronouncements in “No-Way Interactions” are true, but applying them correctly requires understanding the shape of the expected interaction.

  • If you expect the new condition to show a reversal, use a cell n equal to your original study, total N = 2x the original.
  • If you expect the new condition to knock out the effect, use a cell n twice that of your original study, for a total N = 4x the original.
  • If you expect only a 50% attenuation in the new condition, you really ought to use a cell n seven times that of your original study, for a total N = 14x the original! Yes, moderators are harder to show than you might think.

Take-home message: It is not impossible to estimate the effect size of a novel effect, if it builds on a known effect. But you may not like what the estimate has to say about the power of your design.




The Lab-Wise File Drawer

The file drawer problem refers to a researcher failing to publish studies that do not get significant results in support of the main hypothesis. There is little doubt that file-drawering has been endemic in psychology. A number of tools have been proposed to analyze excessive rates of significant publication and suspicious patterns of significance (summarized and referenced in this online calculator). All the same, people disagree about how seriously the file-drawer distorts conclusions in psychology (e.g. Fabrigar & Wegener in JESP, 2016, with comment by Francis and reply). To my mind the greater threat of file-drawering noncompliant studies is ethical. It simply looks bad, has little justification in an age of supplemental materials that shatter the page count barrier, and violates the spirit of the APA Ethics Code.

But I’ll bet that all of us who have been doing research for any time have a far larger file drawer composed of whole lines of research that simply did not deliver significant or consistent results. The ethics here are less clear. Is it OK to bury our dead? Where would we publish whole failed lines of research?

Of course, some research topics are interesting no matter how they come out. As I’ve argued elsewhere, focusing on questions like these would remove a lot of uncertainty from careers and undercut the careerist motivation for academic fraud. But would even the most extreme advocate of open science reform back a hard requirement for a completely transparent lab?

The lab-wise file drawer rate — if you will, the circular file drawer — could explain part or all of publication bias. Statistical power could lag behind the near-unanimous significance of reported results due to whole lines of research being file-drawered. The surviving lines of research, even if they openly report all studies run, would then look better than chance would have it. I ran some admittedly simplistic simulations (Google Drive spreadsheet) to check out how serious the circular file drawer can get.

File, circular, quantity 1


Our simulated lab has eight lines of research going on, testing independent hypotheses with multiple studies. Each study has 50% power to find a significant result given the match between its methods and the actual, population effect size out there. You may think this is low, but keep in mind that even if you build in 80 or 90% power to find, say, a medium sized effect, the actual effect may be small or practically nil, reducing your power post-hoc.

The lab also follows rules for conserving resources while conforming to the standard of evidence that many journals follow. For each idea, they run up to three studies. If two studies fail to get a significant result, they don’t publish the research. They also stop the research short if either they fail to replicate a promising first study, or they try two studies, both of which fail. In this 50% power lab where each study’s success is a coin flip, this means that out of eight lines of research, they will only end up trying to publish three. Sounds familiar?

Remember, all these examples  assume that the lab reports even non-significant studies from lines of research that “succeed” by this standard. There is no topic-wise file drawer — only a lab-wise one.

In our example lab that runs at a consistent 50% power, at the spreadsheet’s top left, the results of this practice look pretty eye-opening. Even though not all reported results are significant, the 77.8% that are significant still exceed the 50% power of the studies. This leads to an R-index of 22, which has been described as a typical result when reporting bias is applied to a nonexistent effect (Schimmack, 2016).


Following the spreadsheet down, we see minimal effects of adopting slightly different rules that are more or less conservative in abandoning a research line after failure. They only require one study more or less about every 4 topics, and the R-indices from these analyses are still problematic.

Following the spreadsheet to the right, we see stronger benefits of carrying out more strongly powered research — which includes studying effects that are more strongly represented in the population to begin with. At 80% power, most research lines yield three significant studies, and the R-index becomes a healthy 71.


The next block to the right assumes only 5% power – a figure that breaks the assumptions of the R index. This represents a lab that is going after an effect that doesn’t exist, so tests will only be significant at the 5% type I error rate. Each of the research rules is very effective in limiting exposure to completely false conclusions, with only one in hundreds of false hypotheses making it to publication.

Before drawing too many conclusions about the 50% power example, however, it is important to question one of its assumptions. If all studies run in a lab have a uniform 50% power, and use similar methods, then all the hypotheses are true, with the same population effect size. Thus, variability in the significance of studies cannot reflect (nonexistent) variability in the truth value of hypotheses.

To reflect reality more closely, we need a model like the one I present at the very far right. A lab uses similar methods across the board to study a variety of hypotheses: 1/3 hypotheses with strong population support (so their standard method yields 80% power), 1/3 with weaker population support (so, 50% power), and 1/3 hypotheses that are just not true at all (so, 5% power). This gives the lab’s publication choices a chance to represent meaningful differences in reality, not just random variance in sampling.

What happens here?


This lab, as expected, flushes out almost all of its tests of nonexistent effects, and finds relatively more success with research lines that have high power based on a strong effect, versus low power based on a weaker effect. As a result, inflation of published findings is still appreciable, but less problematic than if each study is done at a uniform 50% power.

To sum up:

  1. A typical lab might expect to have its published results show inflation above their power levels even if it commits to reporting all studies relevant to each separate topic it publishes on.
  2. This is because of sampling randomness in which topics are “survivors.” The more a lab can reduce this random factor — by running high-powered research, for example — the less lab-wise selection creates inflation in reported results.
  3. A lab’s file drawer creates the most inflation when it tries to create uniform conditions of low power — for example, trying to economize by studying strong effects using weak methods and weak effects using strong methods, so that a uniform post-hoc power of 50% is reached (as in the first example). It may be better to let weakly supported hypotheses wither away (as in the hybrid lab example).

And three additional observations:

  1. These problems vanish in a world where all results are publishable because research is done and evaluated in a way that reflects confidence in even null results (for example, the world of reviewed pre-registration). Psychology is a long way from that world, though.
  2. The labwise file drawer adds another degree of uncertainty when trying to use post-hoc credibility analyses to assess the existence and extent of publication bias. Some of that publication bias may come from the published topic being simply more lucky than other topics in the lab.
  3. If people are going to disagree on the implications, a lot of it will hinge on whether it is ethical to not report failed lines of research. Those who think it’s OK will see a further reason not to condemn existing research, because part of the inflation used as evidence for publication bias could be due to this OK practice. Those who think it’s not OK will press for even more complete reporting requirements, bringing lab psychology more in line with practices in other lab sciences (see illustration).

    Being trusted is a privilege.