About 20 years ago, I was an emotion or affect researcher. I was interested in structural models of affect, which was a hot research topic in the 1980s (Russell, 1980; Watson & Tellegen, 1985; Diener & Iran-Nejad, 1986′ Shaver et al., 1987). In the 1990s, a consensus emerged that the structure of affect has a two-dimensional core, but a controversy remained about the basic dimensions that create the two-dimensional space. One model assumed that Positive Affect and Negative Affect are opposite ends of a single dimension (like hot and cold are opposite ends of a bipolar temperature dimension). The other model assumed that Positive Affect and Negative Affect are independent dimensions. This controversy was never resolved, probably because neither model is accurate (Schimmack & Grob, 2000).

When Seligman was pushing positive psychology as a new discipline in psychology, I was asked to write a chapter for a Handbook of Methods in Positive Psychology. This was a strange request because it is questionable whether Positive Psychology is really a distinct discipline and there are no distinct methods to study topics under the umbrella term positive psychology. Nevertheless, I obliged and wrote a chapter about the relationship between Positive Affect and Negative Affect that questions the assumption that positive emotions are a new and previously neglected topic and the assumption that Positive Affect can be studied separately from Negative Affect. The chapter basically summarized the literature on the relationship between PA and NA up to this point, including some mini meta-analysis that shed light on moderators of the relationship between PA and NA.

As with many handbooks that are expensive and not easily available as electronic documents, the chapter had very little impact on the literature. WebofScience shows only 25 citations. As the topic is still unresolved, I thought I make the chapter available as a free text in addition to the Google Book option that is a bit harder to navigate.

Here is a PDF version of the chapter.

Key points

• The correlation between PA and NA varies as a function of items, response formats, and other method factors.
• Pleasure and displeasure are not opposite ends of a single bipolar dimension
• Pleasure and displeasure are not independent.

The prompt for this essay is my personal experience with accusations of racism in response to my collaboration with my colleague Judith Andersen and her research team who investigated the influence of race on shooting errors in police officers’ annual certification (Andersen, Di Nota, Boychuk, Schimmack, & Collins, 2023a). Our article was heavily criticizes as racially insensitive and racially biased (Williams et al., 2023). We responded to the specific criticisms of our article (Andersen, Di Nota, Boychuk, Schimmack, & Collins, 2003b). This essay is takes a broader perspective on the study of race-related topics in psychological science. It is also entirely based on my own experiences and views and I do not speak for my colleagues.

Science

The term science is used to distinguish claims that are backed-up by scientific facts from claims that are based on other evidence or belief systems. For people who believe in science, these claims have a stronger influence on their personal belief systems than other claims. Take “flat-earth theorists” as an example. Most educated people these days believe that the Earth is round and point to modern astronomy as a science that supports this claim. However, some people seriously maintain the belief that the earth is flat (https://en.wikipedia.org/wiki/Behind_the_Curve). Debates between individuals or groups who “follow the science” or not are futile. In this regard, believing in science is like a religion. This article is addressed at readers who “believe in science.”

What does it mean to believe in science? A fundamental criterion that distinguishes science from other belief systems is falsifiability. At some point, empirical evidence has to be able to correct pre-existing beliefs. For this to happen, the evidence has to be strong. For example, there should be little doubt about the validity of the measures (e.g., thermometers are good measures of temperature) and the replicability of the results (different research teams obtain the same results). When these preconditions are fulfilled, scientific discoveries are made and knowledge is gained (e.g., better telescopes produce new discoveries in astronomy, microscopes showed the influence of bacteria on diseases, etc.). The success of Covid-19 vaccines (if you believe in science) was possible due to advances in microbiology. The modern world we live in would not exist without actions by individuals who believe in science.

Psychological Science

Psychological science emerged in the late 19th century as an attempt to use the scientific method to study human experiences and behavior. The biggest success stories in psychological science can be found in areas that make it possible to conduct tightly controlled laboratory studies. For example, asking people to read color words in the same color or a different color shows a robust effect that it is harder to name color of a color word if the color word does not match (say purple when the word purple is printed in green).

Psychological science of basic phenomena like perception and learning has produced many robust scientific findings. Many of these findings are so robust because they are universal; that is, shared by all humans. This is consistent with other evidence that humans are more alike than different from each other and that peripheral differences like height, hair texture, and pigmentation are superficial differences and not symptoms of clearly distinguishable groups of humans (different races).

Social Psychology

Social psychology emerged as a sub-discipline in psychological science in the 1950s. A major goal of social psychology was to use the methods of psychological science to study social behaviors with bigger social implications than the naming of colors. The most famous studies from the 1950 tried to explain the behavior of Germans during World War II who were involved in the Holocaust. The famous Milgram experiments, for example, showed that social pressure can have a strong influence on behavior. Asch showed that conformity pressure can make people say things that are objectively false. These studies are still powerful today because they used actual behaviors as the outcome. In Milgram’s studies participants were led to believe that they gave electro shocks to another person who screamed in pain.

From the beginning, social psychologists were also interested in prejudice (Allport, 1954), at a time when the United States were segregated and blatantly racist. White Americans’ racial attitudes were easy to study because White Americans openly admitted that they did not consider White and Black Americans to be equal. For example, in the 1950s, nearly 100% of Americans disapproved of interracial marriages, which were also illegal in some states at that time.

It was more difficult to study the influence of racism on behavior. To ensure that behavior is influenced by an individual’s race and not some other factor (psychology jargon for cause), it is necessary to keep all other causes constant and then randomly assign participants to the two conditions and show a difference in outcome. My search for studies of this type revealed only a handful of studies with small student samples that showed no evidence of prejudice (e.g., Genthner & Taylor, 1973). There are many reasons why these studies may have failed to produce evidence of prejudice. For example, participants knew that they were in a study and that their behaviors were observed, which may have influenced how they behaved. Most important is the fact that the influence of prejudice on behavior was not a salient topic in social psychology.

This changed in the late 1980s (at a time when I became a student of psychology), when social psychologists became interested in unconscious processes that were called implicit processes (Devine, 1989). The novel idea was that racial biases can influence behavior outside of conscious awareness. Thus, some individuals might claim that they have no prejudices, but their behaviors show otherwise. Twenty years later, this work led to the claim that most White people have racial biases that influence their behavior even if they do not want to (Banaji & Greenwald, 2013).

Notably, in the late 1980s, 40% of US Americans still opposed interracial marriages, showing that consciously accessible, old fashioned racism was still prevalent in the United States. However, the primary focus of social psychologists was not the study of prejudice, but the study of unconscious/implicit processes, implicit prejudice was just one of many implicit topics that were being the topic of investigation.

While the implicit revolution led to hundreds of studies that examined White people’s behaviors in responses to Black and White persons, the field also made an important methodological change. Rather than studying real behaviors to real people, most studies examined how fast participants can press a button in response to a stimulus (e.g. a name, a face, or simply the words Black/White) on a computer screen. The key problem with this research is that button presses on computer screens are not the same as button presses on dating profiles or pressing the trigger on a gun during a use of force situation.

This does not mean that these studies are useless, but it is evident that they cannot produce scientific evidence about the influence of race on behavior in the real world. In the jargon of psychological science, these studies lack external validity (i.e., the results cannot be generalized from button presses in computer tasks to real world behaviors).

Psychological Science Lacks Credibility

Psychology faces many challenges to be recognized as a science equal to physics, chemistry, or biology. One major challenge is that the behaviors of humans vary a lot more than the behaviors of electrons, atoms, or cells. As a result, many findings in social psychology are general trends that explain only a small portion of the variability in behavior (e.g., some White people are in interracial relationships). To deal with this large amount of variability (noise, randomness), psychologists rely on statistical methods that aim to detect small effects on the variability in behavior. Since the beginning of psychological science, the statistical method to find these effects is a statistical method called null-hypothesis significance testing or simply significance testing (Is p < .05?). Although this method has been criticized for decades, it continues to be taught to undergraduate students and is used to make substantive claims in research articles.

The problem with significance testing is that it is designed to confirm researchers’ hypotheses, but it cannot falsify them. Thus, the statistical tool cannot serve the key function of science to inform researchers that they ideas are wrong. As researchers are human and humans already have a bias to find evidence that supports their beliefs, significance testing is an ideal tool for scientists to delude themselves that their claims are supported by scientific evidence (p < .,05), when their beliefs are wrong.

Awareness of this problem increased after a famous social psychologist, Daryl Bem, used NHST to convince readers that humans have extrasensory perception and can foresee future events (Bem, 2011). Attesting to the power of confirmation bias, Bem still believes in ESP, but the broader community has realized that the statistical practices in social psychology are unscientific and that decades of published research lacks scientific credibility. It did not help that a replication project found that only 25% of published results in the most prestigious journals of social psychology could be replicated.

Despite growing awareness about the lack of credible scientific evidence, claims about prejudice and racism in textbooks, popular books, and media articles continue to draw on this literature because there is no better evidence (yet). The general public and undergraduate students make the false assumption that social psychologists are like astronomers who are interpreting the latest pictures from the new space telescope. Social psychologists are mainly presenting their own views as if they were based on scientific evidence, when there is no scientific evidence to support these claims. This explains why social psychologists often vehemently disagree about important issues. There is simply no shared empirical evidence that resolves these conflicts.

Thus, the disappointing and honest answer is that social psychology simply cannot provide scientific answers to real world questions about racial biases in behavior. Few studies actually examined real behavior, studies of button presses on computers have little ecological validity, and published results are often not replicable.

The Politicization of Psychological Science

In the absence of strong and unambiguous scientific evidence, scientists are no different from other humans and confirmation biases will influence scientist’s beliefs. The problem is that the general public confuses their status as university professors and researchers with expertise that is based on superior knowledge. As a result, claims by professors and researchers in journal articles or in books, talks, or newspaper interviews are treated as if they deserve more weight than other views. Moreover, other people may refer to the views of professors or their work to claim that their own view are scientific because they echo those printed in scientific articles. When these claims are not backed by strong scientific evidence, scientific articles become weaponized in political conflicts.

A scientific article on racial biases in use of force errors provides an instructive example. In 2019, social psychologist Joseph Cesario and four graduate students published an article on racial disparities in use of force errors by police (a.k.a., unnecessary killings of US civilians). The article passed peer-review at a prestigious scientific journal, the Proceedings of the National Academy of Sciences (PNAS). Like many journals these days, PNAS asks authors to provide a Public Significance Statement.

The key claim in the significance statement is that the authors found “no evidence of anti-Black or anti-Hispanic disparities across shootings.” Scientists may look at this statement and realize that it is not equivalent to the claim that “there is no racial bias in use of force errors.” First of all, the authors clearly say that they did not find evidence. This leaves the possibility that other people looking at the same data might have found evidence. Among scientists it is well known that different analyses can produce different results. Scientists also know the important distinction between the absence of evidence and evidence of the absence of an effect. The significance statement does not say that the results show that there are no racial biases, only that the authors did not find evidence for biases. However, significance statements are not written for scientists and it is easy to see how these statement could be (unintentionally or intentionally) misinterpreted as saying that science shows that there are no racial biases in police killings of innocent civilians.

And this is exactly what happened. Black-Lives-Anti-Matter Heather Mac Donald, used this research as “scientific evidence” to support the claim that the liberal left is fighting an unjustified “War on Cops” Her bio on Wikipedia shows that she received degrees in English, without any indication that she has a background in science. Yet, the Wall Street journal allowed her to summarize the evidence in an opinion article with the title “The myth of systemic police racism.” Thus, a racially biased and politically motivated non-scientist was able to elevate her opinion by pointing to the PNAS article as evidence that her opinion is the truth.

In this particular case, the journal was forced to retract the article after post-publication peer-reviewed revealed statistical errors in the paper and it became clear that the significance statement was misleading. An editorial reviewed this case-study of politicized science in great detail (Massey & Waters, 2020).

Although this editorial makes it clear that mistakes were made, it doesn’t go far enough in admitting the mistakes that were made by the journal editors. Most important, even if the authors had not made mistakes, it would be wrong to allow for any generalized conclusions in a significance statement. The clearest significance statement would be that “This is only one study of the issue with limitations and the evidence is insufficient to draw conclusions based on this study alone.” But journals are also motivated to exaggerate the importance of articles to increase their prestige.

The editorial also fails to acknowledge that the authors, reviewers, and editor were White and that it is unlikely that the article would have made misleading statements if African American researchers were involved in the research, peer-review, or the editorial decision process. To African Americans the conclusion that there is no racial bias in policing is preposterous, while it seemed plausible to the White researchers who gave the work the stamp of approval. Thus, this case study also illustrates the problems of systemic racism in psychology that African Americans are underrepresented and often not involved in research that directly affects them and their community.

My Colleague’s Research with Police Officers

My colleague, Judith Andersen, is a trained health psychologist, with a focus on stress and health. One area of research is how police officers cope with stress and traumatic experiences they encounter in their work. This research put her in a unique position to study racial biases in the use of force with actual police officers (i.e., many social psychologists studied shooting games with undergraduate students). Getting the cooperation of police department and individual officers to study such a highly politicized topic is not easy and without cooperation there are no PARTICIPANTS, no data, and no scientific evidence. A radical response to this reality would be to reject any data that require police officers’ consent. That is a principled response, but not a criticism of researchers who conduct studies and note the requirement of consent as a potential limitation and refrain from making bold statements that their data settle a political issue.

The actual study is seemingly simple. Officers have to pass a use of force test for certification to keep their service weapon on duty. To do so, officers go through a series of three realistic scenarios with their actual service weapon and do not know whether “shoot” or “don’t shoot” is the right response. Thus, they may fail the test if they fail to shoot in scenarios where shooting is the right response. The novel part of the study was to create two matched scenarios with a White or Black suspect and randomly assigned participating officers to these scenarios. Holding all other possible causes constant make it possible to see whether shooting errors are influenced by the race of a suspect.

After several journals, including PNAS, showed no interest in this work, it was eventually accepted for publication by the editor of The Canadian Journal of Behavioural Science. The journal also requires a Significance statement and we provided one.

Scientists might notice that our significance statement is essentially identical to Johnson et al.’s fateful significance statement. In plain English, we did not find evidence of racial biases in shooting errors. The problem is that significance testing often lead to the confusion of lack of evidence and evidence of no bias. To avoid this misinterpretation, we made it clear that our results cannot be interpreted as evidence that there are no biases. To do so, we emphasized that the shooting errors in the sample did show a racial bias. However, we could not rule out that this bias was unique to this sample and that the next sample might show no bias or even the opposite bias. We also point out that the bias in this sample might be smaller than the actual bias and that the actual bias might fully account for the real world disparities. In short, our significance statement is an elaborate, jargony way of saying “our results are inconclusive and have no real-world significance.”

It is remarkable that the editor published our article because 95% of articles in psychology present a statistically significant result that justifies a conclusion. This high rate of successful studies, however, is a problem because selective publishing of only significant results undermines the credibility of published results. Even cray claims like mental time travel are supported by statistically significant results. Only the publication of studies that failed to replicate these results help us to see that the original results were wrong. It follows that journals have to publish articles with inconclusive results to be credible and researchers have to be allowed to present inconclusive results to ensure that conclusive results are trustworthy. It also follows that not all scientific articles are in need of media attention and publicity. The primary aim of scientific journals is communication among scientists and to maintain a record of scientific results. Even Nadal or Federer did not win every tournament. So, scientists should be allowed to publish articles that are not winners and nobody should trust scientists who only publish articles that confirm their predictions.

It is also noteworthy that our results were inconclusive because the sample size was too small to draw stronger conclusions. However, it was the first study of its kind and it was already a lot of effort to get even these data. The primary purpose of publishing a study like this is to stimulate interest and to provide an example for future studies. Eventually, the evidence base grows and more conclusive results could be obtained. Ultimately it is up to the general public and policy makers to fund this research and to require participation of police departments in studies of racial bias. It would be foolish to criticize our study because it didn’t produce conclusive results in the first investigation. Even if the study had produced statistically significant results, replication studies would be needed before any conclusions can be drawn.

Social Activism in Science

Williams et al. (2023) wrote a critical commentary of our article with the title “Performative Shooting Exercises Do Not Predict Real-World Racial Bias in Police Officers” We were rather surprised by this criticism because our main finding was basically a non-significant, inconclusive result. Apparently, this was not the result that we were supposed to get or we should not have reported these results that contradict Williams et al.’s beliefs. Williams et al. start with the strong belief that any well-designed scientific study must find evidence for racial biases in shooting errors; otherwise there must be a methodological flaw. They are not shy to communicate this belief in their title. Our study of shooting errors during certification are called performative and they “do not predict real world racial biases in police officers.” The question is how Williams et al. (2023) know the real-world racial biases of police officers to make this claim.

The answer is that they do not know anything more than anybody else about the real racial biases of police officers (You are invited to read the commentary and see whether I missed that crucial piece of information). Their main criticism is that we made unjustified assumptions about the external validity of the certification task. “The principal flaw with Andersen et al.’s (2023) paper is unscientific assumptions around the validity of the recertification shooting test” That is, the bias that we observed in the certification task is taken at face value as information about the bias in real-world shooting situations.

The main problem with this criticism is that we never made the claim that biases in the certification task can be used to draw firm conclusions about biases in the real world. We even pointed out that we observed biases and that our results are consistent with the assumption that all of the racial disparities in real-world shootings are caused by racial biases in the immediate shooting decisions. As it turns out, Williams et al.’s critique is unscientific because it makes unscientific claims in the title and misrepresents our work. Our real sin was to be scientific and to publish inconclusive results that do not fit into the narrative of anti-police leftwing propaganda.

It is not clear why the authors were allowed to make many false and hurtful statements in their commentary, but personally I think it is better to have this example of politicization in the open to show that left-wing and right-wing political activists are trying to weaponize science to elevate their beliefs to the status of truth and knowledge.

Blatant examples of innocent African Americans killed by police officers (wikipedia) are a reason to conduct scientific studies, but these incidences cannot be used to evaluate the scientific evidence. And without good science, resources might be wasted on performative implicit bias training sessions that only benefit the trainers and do not protect the African American community.

Conclusion

The simple truth remains that psychological science has done little to answer real-world questions around race. Although social psychology has topics like prejudice and intergroup relationships as core topics, the research is often too removed from the real world to be meaningful. Unfortunately, incentives reward professors to use the inconclusive evidence selectively to confirm their own beliefs and then to present these beliefs as scientific claims. These pseudo-scientific claims are then weaponized by like-minded ideologues. This creates the illusion that we have scientific evidence, which is contradicted by the fact that opposing camps both cite science to believe they are right just like opposing armies can pray to the same God for victory.

To change this, stakeholders in science, like government funding organizations, need to change the way money is allocated. Rather than giving grants to White researchers at elite universities to do basic (a.k.a., irrelevant) research on button-presses of undergraduate students, money should be given to diverse research teams with a mandate to answer practical, real-world questions. The reward structure at universities also has to change. To collect real world data from 150 police officers is 100 times more difficult than collecting 20 brain measures from undergraduate students. Yet, a publication in a neuroscience journal is seen as more scientific and prestigious than an article in journal that addresses real-world problems that are by nature of interest to smaller communities.

Finally, it is important to recognize that a single study cannot produce conclusive answers to important and complex questions. All the major modern discoveries in the natural (real) sciences are made by teams. Funders need to provide money for teams that work together on a single important question rather than funding separate labs who work against each other. This is not new and has been said many times before, but so far there is little evidence of change. As a result, we have more information about galaxies millions of years ago than about our own behaviors and the persistent problem of racism in modern society. Don’t look to the scientists to provide a solution. Real progress has and will come from social activists and political engagement. And with every generation, more old racists will be replaced by a more open new generation. This is the way.

“Instead of a scientist entering the environment in search of the truth, we find the rather unflattering picture of a charlatan trying to make the data come out in a manner most advantageous to his or her already-held theories” (p. 88).  [Fiske & Taylor, 1984)

A critical examination of Miller and Ulrich’s article “Optimizing Research Output:
How Can Psychological Research Methods Be Improved?” (https://doi.org/10.1146/annurev-psych-020821-094927)

Introduction

Meta-science has become a big business over the past decade because science has become a big business. With the increase in scientific production and the minting of Ph.D. students, competition has grown and researchers are pressured to produce ever more publications to compete with each other. At the same time, academia still pretends that it plays by the rules of English lords with “peer”-review and a code of honor. Even outright fraud is often treated like jaw-walking.

The field of meta-science puts researchers’ behaviors under the microscope and often reveals shady practices and shoddy results. However, meta-scientists are subject to the same pressures as the scientists they examine. They get paid, promoted, and funded based on the quantity of their publications, and citations. It is therefore reasonable to ask whether meta-scientists are any more trustworthy than other scientists. Sadly, that is not the case. Maybe this is not surprising because they are human like everybody else. Maybe the solution to human biases will be artificial intelligence programs. For now, the only way to reduce human biases is to call them out whenever you see them. Meta-scientists do not need meta-meta-scientists to hold them accountable, just like meta-scientists are not needed to hold scientists accountable. In the end, scientists hold each other accountable by voicing scientific criticism and responding to these criticisms. The key problem is that open exchange of arguments and critical discourse is often lacking because insiders use peer-review and other hidden power structures to silence criticism.

Here I want to use the chapter “Optimizing Research Output: How Can Psychological
Research Methods Be Improved?” by Jeff Miller and Rolf Ulrich as an example of biased and unscientific meta-science. The article was published in the series “Annual Reviews of Psychology” that publishes invited review articles. One of the editors is Susan Fiske, a social psychologists who once called critical meta-scientists like me “method terrorists” because they make her field look bad. So far, this series has published several articles on the replication crisis in psychology with titles like “Psychology’s Renaissance.” I was never asked to write or review any of these articles, although I have been invited to review articles on this topic by several editors of other journals. However, Miller and Ulrich did cite some of my work and I was curious to see how they cited it.

Consistent with the purpose of the series, Miller and Ulrich claim that their article provides “a (mostly) nontechnical overview of this ongoing metascientific work.” (p. 692). They start with a discussion of possible reasons for low replicability.

2. WHY IS REPLICABILITY SO POOR?

The state “there is growing consensus that the main reason for low replication rates is that many original published findings are spurious” (p. 693).

To support this claim they point out that psychology journals mostly publish statistically significant results (Sterling, 1959; Sterling et al., 1959), and then conclude “current evidence of low replication rates tends to suggest that many published findings are FPs [false positives] rather than TPs.[true positives]. This claim is simply wrong because it is very difficult to distinguish false positives from true positives with very low power to produce a significant result. They do not mention attempts to estimate the false positive rate (Jager & Leek, 2014; Gronau et al., 2016; Schimmack & Bartos, 2021). These methods typically show low to moderate estimates of the false positive rate and do not justify the claim that most replication failures occur when an article reported a false positive result.

Miller and Ulrich now have to explain how false positive results can enter the literature in large numbers when the alpha criterion of .05 is supposed to keep most of these results out of publications. The propose that many “FPs [false positive] may reflect honest research errors at many points during the research process” (p. 694). This argument ignores the fact that concerns about shady research practices first emerged when Bem (2011) published a 9 study article that seemed to provide evidence for pre-cognition. According to Miller and Ulrich we have to believe that Bem made 9 honest errors in a row that miraculously produced evidence for his cherished hypothesis that pre-cognition is real. If you believe this is possible, you do not have to read further and I wish you a good life. However, if you share my skepticism, you might feel relieved that there is actually meta-scientific evidence that Bem used shady practices to produce his evidence (Schimmack, 2018).

3. STATISTICAL CAUSES OF FALSE POSITIVES

Honest mistakes alone cannot explain a high percentage of false positive results in psychology journals. Another contributing factor has to be that psychologists test a lot more false hypotheses than true hypotheses. Miller and Ulrich suggest that social psychologists test only 1 out of 10 hypotheses tests tests a true hypothesis. Research programs with such a high rate of false hypotheses are called high-risk. However, this description does not fit the format of typical social psychology articles that have lengthy theory sections and often state “as predicted” in the results section, often repeatedly for similar studies. Thus, there is a paradox. Either social psychology is risky and results are surprising or it is theory-driven and results are predicted. It cannot be both.

Miller and Ulrich ignore the power of replication studies to reveal false positive results. This is not only true in articles with multiple replication studies, but across different articles that publish conceptual replication studies of the same theoretical hypothesis. How is it possible that all of these conceptual replication studies produced significant results, when the hypothesis is false? The answer is that researchers simply ignored replication studies that failed to produce the desired results. This selection bias, also called publication bias, is well-known and never called an honest mistake.

All of this gaslighting serves the purpose to present social psychologists as honest and competent researchers. High false positive rates and low replication rates happen “for purely statistical reasons, even if researchers use only the most appropriate scientific methods.” This is bullshit. Competent researchers would not hide non-significant results and continue to repeatedly test false hypotheses, while writing articles that claim all of the evidence supports their theories. Replication failures are not an inevitable statistical phenomenon. They are man-made in the service of self-preservation during early career stages and ego-preservation during later ones.

4. SUGGESTIONS FOR REDUCING FALSE POSITIVES

Conflating false positives and replication failures, Miller and Ulrich review suggestions to improve replication rates.

4.1. Reduce the α Level

One solution to reducing false positive results is to lower the significance threshold. An influential article called for alpha to be set to .005 (1 out of 200 tests can produce a false positive result). However, Miller and Ulrich falsely cite my 2012 article in support of this suggestion. This ignores that my article made a rather different recommendation, namely to conduct fewer studies with a higher probability to provide evidence for a true hypothesis. This would also reduce the false positive rate without having to lower the alpha criterion. Apparently, they didn’t really read or understand my article.

4.2 Eliminate Questionable Research Practices

A naive reader might think that eliminating shady research practices should help to increase replication rates and to reduce false positive rates. For example, if all results have to be published, researchers would think twice about the probability of obtaining a significant results. Which sane researcher would test their cherished hypothesis twice with 50% power; that is, the probability of finding evidence for it. Just like flipping a coin twice, the chance of getting at least one embarrassing non-significant result would be 75%. Moreover, if they had to publish all of their results, it would be easy to detect hypotheses with low replication rates and either give up on them or increase sample sizes to detect small effect sizes. Not surprisingly, consumers of scientific research (e.g., undergraduate students) assume that results are reported honestly and scientific integrity statements often imply that this is the norm.

However, Miller and Ulrich try to spin this topic in a way that suggests shady practices are not a problem. They argue that shady practices are not as harmful as some researchers have suggested, citing my 2020 article, because “because QRPs also increase power by making it easier to reject null hypotheses that are false as well as those that are true (e.g., Ulrich & Miller 2020).” Let’s unpack this nonsense in more detail.

Yes, questionable researcher practices increase the chances of obtaining a significant result independent of the truth of the hypothesis. However, if researchers test only 1 true hypotheses for every 9 false hypotheses, QRPs can have a much more sever effect on the rate of significant results when the null-hypothesis is false. Also a false hypotheses starts with a low probability of a significant result when researchers are honest, namely 5% with the standard criterion of significance. In contrast, a true hypothesis can have anywhere between 5% and 100% power, limiting the room for shady practices to inflate the rate of significant results when the hypothesis is true. In short, the effect of shady practices are not equal and false hypotheses benefit more from shady practices than true hypotheses.

The second problem is that Miller and Ulrich conflate false positives and replication failures. Shady practices in original studies will also produce replication failures when the hypothesis is true. The reason is that shady practices lead to inflated effect size estimates, while the outcome of the honest replication study is based on the true population effect size. As this is often 50% smaller than the inflated estimates in published articles, replication studies with similar sample sizes are bound to produce non-significant results (Open Science Collaboration, 2015). Again, this is true even if the hypothesis is true (i.e., the effect size is not zero).

4.3 Increase Power

As Miller and Ulrich point out, increasing power has been a recommendation to improve psychological science (or a recommendation for psychology to become a science) for a long time (Cohen, 1961). However, they point out that this recommendation is not very practical because “it is very difficult to say what sample sizes are needed to attain specific target
power levels, because true effect sizes are unknown” (p. 698). This argument against proper planning of sample sizes is false for several reasons.

First, I advocated for higher power in the context of multi-study papers. Rather than conducting 5 studies with 20% power, researchers should use their resources to conduct one study with 80% power. The main reason researchers do not do this is that the single study might still not produce a significant result and they are allowed to hide underpowered studies that failed to produce a significant result. Thus, the incentive structure that rewards publication of significant results rewards researchers who conduct many underpowered studies and only report those that worked. Of course, Miller and Ulrich avoid discussing this reason for the lack of proper power analysis to maintain the image that psychologists are honest researchers with the best intentions.

Second, researchers do not need to know the population effect size to plan sample sizes. One way to plan future studies is to base the sample size on previous studies. This is of course what researchers have been doing only to find out that results do not replicate because the original studies used shady practices to produce significant results. Many graduate students who left academia spent years of their Ph.D. trying to replicate published findings and failed to do so. However, all of these failures remain hidden so that power analyses based on published effect sizes lead to more underpowered studies that do not work. Thus, the main reason why it is difficult to plan sample sizes is that the published literature reports inflated effect sizes that imply small samples are sufficient to have adequate power.

Finally, it is possible to plan studies with the minimal effect size of interest. These studies are useful because a non-significant result implies that the hypothesis is not important even if the strict nil-hypothesis is false. The effect size is just so small that it doesn’t really matter and requires extremely large effect sizes to study them. Nobody would be interested in doing studies on this irrelevant effects that require large resources. However, to know that the population (true) effect size is too small to matter, it is important to conduct studies that are able to estimate small effect sizes precisely. In contrast, Miller and Ulrich warn that sample sizes could be too large because large samples “provide high power to detect effects that are too small to be of practical interest”. (p. 698). This argument is rooted in the old statistical approach to ignore effect sizes and be satisfied with a conclusion that the effect size is not zero, p < .05, what Cohen called nil-hypothesis testing and others have called a statistical ritual. Sample sizes are never too large because larger samples provide more precision in the estimation of effect sizes, which is the only way to establish that a true effect size is too small to be important. A study that define the minimum effect size of interest and uses this effect size as the null-hypothesis can determine whether the effect is relevant or not.

4.4. Increase the Base Rate

Increasing the base rate means testing more true hypotheses. Of course, researchers do not know a priori which hypotheses are true or not. Otherwise, the study would not be necessary (actually many studies in psychology test hypotheses where the null-hypothesis is false a priori, but that is a different issue). However, hypotheses can be more or less likely to be true based on exiting knowledge. For example, exercise is likely to reduce weight, but counting backwards from 100 to 1 every morning is not likely to reduce weight. Many psychological studies are at least presented as tests of theoretically derived hypotheses. The better the theory, the more often a hypothesis is true and a properly powered study will produce a true positive result. Thus, theoretical progress should increase the percentage of true hypotheses that are tested. Moreover, good theories would even make quantitative predictions about effect sizes that can be used to plan sample sizes (see previous section).

Yet, Miller and Ulrich conclude that “researchers have little direct control over their base
rates” (p. 698). This statement is not only inconsistent with the role of theory in the scientific process, it is also inconsistent with the nearly 100% success rate in published articles that always show the predicted results, if only because the prediction was made after the results were observed rather than from an a priori theory (Kerr, 1998).

In conclusion, Miller and Ulrich’s review of recommendations is abysmal and only serves the purpose to exonerate psychologists from justified accusations that they are playing a game that looks like science, but is not science, because researchers are rewarded for publishing significant results that fail to provide evidence for hypotheses because even false hypotheses produce significant results with the shady practices that psychologists use.

5. OBJECTIONS TO PROPOSED CHANGES

Miller and Ulrich start this section with the statement that “although the above suggestions for reducing FPs all seem sensible, there are several reasonable objections to them” (p. 698). Remember one of the proposed changes was to curb the use of shady practices. According to Miller and Ulrich there is a reasonable objection to this recommendation. However, what would be a reasonable objection to the request that researchers should publish all of their data, even those that do not support their cherished theory? Every undergraduate student immediately recognizes that selective reporting of results undermines the essential purpose of science. Yet, Miller and Ulrich want readers to believe that there are reasonable objections to everything.

“Although to our knowledge there have been no published objections to the idea that QRPs should be eliminated to hold the actual Type 1 error rate at the nominal α level, even this
suggestion comes with a potential cost. QRPs increase power by providing multiple opportunities to reject false null hypotheses as well as true ones” (p. 699).

Apparently, academic integrity only applies to students, but not to their professors when they go into the lab. Dropping participants, removing conditions, dependent variables, or entire studies, or presenting exploratory results as if they were predicted a priori are all ok because these practices can help to produce a significant result even when the nil-hypothesis is false (i.e., there is an effect).

This absurd objection has several flaws. First, it is based on the old and outdated assumption that the only goal of studies is to decide whether there is an effect or not. However, even Miller and Ulrich earlier acknowledged that effect sizes are important. Sometimes effect sizes are too small to be practically important. What they do not tell their readers is that shady practices produce significant results by inflating effect sizes, which can lead to the false impression that the true effect size is large, when it is actually tiny. For example, the effect size of an intervention to reduce implicit bias on the Implicit Association Test was d = .8 in a sample of 30 participants and shrank to d = .08 in a sample of 3,000 participants (cf. Schimmack, 2012). What looked like a promising intervention when shady practices were used, turned out to be a negligible effect in an honest attempt to investigate the effect size.

The other problem is of course that shady practices can produce significant results when a hypothesis is true and when a hypothesis is false. If all studies are statistically significant, statistical significance no longer distinguishes between true and false hypotheses (Sterling, 1959). It is therefore absurd to suggest that shady practices can be beneficial because they can produce true positive results. The problem of shady practices is the same problem as a liar. They sometimes say something true and sometimes they lie, but you don’t know when they are honest or lying.

9. CONCLUSIONS

The conclusion merely solidifies Miller and Ulrich’s main point that there are no simple recommendations to improve psychological science. Even the value of replications can be debated.

“In a research scenario with a 20% base rate of small effects (i.e., d = 0.2), for example, a researcher would have the choice between either running a certain number of large studies with α = 0.005 and 80% power, obtaining results that are 97.5% replicable, or running six times as many small studies with α = 0.05 and 40% power, obtaining results that are 67% replicable. It is debatable whether choosing the option producing higher replicability would necessarily result in the fastest scientific progress.”

Fortunately, we have a real example of scientific progress to counter Miller and Ulrich’s claim that fast science leads to faster scientific progress. The lesson comes from molecular genetics research. When it became possible to measure variability in the human genome, researchers were quick to link variations in one specific gene to variation in phenotypes. This candidate gene research produced many significant results. However, unlike psychological scientists journals in this area of research also published replication failures and it became clear that discoveries could often not be replicated. This entire approach has been replaced by collaborative projects that rely on very large data sets and many genetic predictors to find relationships. Most important, they reduced the criterion for significance from .05 to .000000005 to increase the ratio of true positives and false positives. The need for large samples slows down this research, but at least this approach has produced some solid findings.

In conclusion, Miller and Ulrich pretend to engage in a scientific investigation of scientific practices and a reasonable discussion of their advantages and disadvantages. However, in reality they are gaslighting their readers and fail to point out a simple truth about science. Science is build on trust and trust requires honest and trustworthy behavior. The replication crisis in psychology has revealed that psychological science is not trustworthy because researchers use shady practices to support their cherished theories. While they pretend to subject their theories to empirical tests, the tests are a sham and rigged in their favor. The researcher always wins because they have control over the results that are published. As long as these shady practices persist, psychology is not a science. Miller and Ulrich disguise this fact in a seemingly scientific discussion of trade-offs, but there is no trade-off between honesty and lying in science. Only scientists who report all of their data and analyses decision can be trusted. This seems obvious to most consumers of science, but it is not. Psychological scientists who are fed up with the dishonest reporting of results in psychology journals created the term Open Science to call for transparent reporting and open sharing of data, but these aspects of science are integral to the scientific method. There is no such thing as closed science where researchers go to their lab and then present a gold nugget and claim to have created it in their lab. Without open and transparent sharing of the method, nobody should believe them. The same is true for contemporary psychology. Given the widespread use of shady practices, it is necessary to be skeptical and to demand evidence that shady practices were not used.

It is also important to question the claims of meta-psychologists. Do you really think it is ok to use shady practices because they can produce significant results when the nil-hypothesis is false? This is what Miller and Ulrich want you to believe. If you see a problem with this claim, you may wonder what other claims are questionable and not in the best interest of science and consumers of psychological research. In my opinion, there is no trade-off between honest and dishonest reporting of results. One is science, the other is pseudo-science. But hey, that is just my opinion and the way the real sciences work. Maybe psychological science is special.

This blog post is a review of a manuscript that hopefully will never be published, but it probably will be. In that case, it is a draft for a PubPeer comment. As the ms. is under review, I cannot share the actual ms., but the review makes clear what the authors are trying to do.

Review

I assume that I was selected as a reviewer for this manuscript because the editor recognized my expertise in this research area.  While most of my work on replicability has been published in the form of blog posts, I have also published a few peer-reviewed publications that are relevant to this topic. Most important, I have provided estimates of replicability for social psychology using the most advanced method to do so, z-curve (Bartos & Schimmack, 2020; Brunner & Schimmack, 2020), using the extensive coding by Motyl et al. (2017) (see Schimmack, 2020).  I was surprised that this work was not mentioned.

In contrast, Yeager et al.’s (2019) replication study of 12 experiments is cited and as I recall 11 of the 12 studies replicated successfully. So, it is not clear why this study is cited as evidence that replication attempts often “producing pessimistic results”

While I agree that there are many explanations that have been offered for replication failures, I do not agree that listing all of these explanations is impossible and that it is reasonable to focus on some of these explanations, especially if the main reason is left out. Namely, the main reason for replication failures is that original studies are conducted with low statistical power and only those that achieve significance are published (Sterling et al., 1995; Schimmack, 2020).  Omitting this explanation undermines the contribution of this article.

The listed explanations are

(1) original articles making use of questionable research practices that result in Type I errors

This explanation conflates two problems. QRPs are used to get significance when power to do so is low, but we do not know whether the population effect size is zero (type-I error) or above zero (type-II error).

(2) original research’s pursuit of counterintuitive findings that may have lower a priori probabilities and thus poor chances at replication

This explanations assumes that there are a lot of type-I errors, but we don’t really know whether the population effect size is zero or not. So, this is not a separate explanation, but rather an explanation why we might have many type-I errors assuming that we do have many type-I errors, which we do not know.

(3) the presence of unexamined moderators that produce differences between original and replication research (Dijksterhuis, 2014; Simons et al., 2017),

This citation ignores that empirical tests of this hypothesis have failed to provide evidence for it (van Bavel et al., 2016).

4) specific design choices in original or replication research that produce different conclusions (Bouwmeester et al., 2017; Luttrell et al., 2017; Noah et al., 2018).

This argument is not different from (3). Replication failures are attributed to moderating factors that are always possible because exact replications are impossible.

To date, discussions of possible explanations for poor replication have generally been presented as distinct accounts for poor replication, with little attempt being made to organize them into a coherent conceptual framework. 

This claim ignores my detailed discussion of the various explanations including some not discussed by the authors (Schooler decline effect; Fiedler, regression to the mean; Schimmack, 2020).

The selection of journals is questionable. Psychological Science is not a general (meta)-psychological journal. Instead there are two journals, The Journal of General Psychology and Meta-Psychology that contain relevant articles.

The authors then introduce Cook and Campbell’s typology of validity and try to relate it to accounts of replication failures based on some work by Fabrigar et al. (2020). This attempt is flawed because validity is a broader construct than replicability or reliability.  Measures can be reliable and correlations can be replicable even if the conclusions drawn from these findings are invalid. This is Intro Psych level stuff.

Statistical conclusion validity is concerned with the question of “whether or not two or more variables are related.”  This is of course nothing else than the distinction between true and false conclusions based on significant or non-significant results.  As noted above, even statistical conclusion validity is not directly related to replication failures because replication failures do not tell us whether the population effect size is zero or not.  Yet, we might argue that there is a risk of false positive conclusions when statistical significance is achieved with QRPs and these results do not replicate. So, in some sense statistical conclusion validity is tied to the replication crisis in experimental social psychology.

Internal validity is about the problem of inferring causality from correlations. This issue has nothing to do with the replication crisis because replication failures can occur in experiments and correlational studies. The only indirect link to internal validity is that experimental social psychology prided itself on the use of between-subject experiments to maximize internal validity and minimize demand effects, but often used ineffective manipulations (priming) that required QRPs to get significance especially in the tiny samples that were used because experiments are more time-consuming and labor intensive. In contrast, survey studies often are more replicable because they have larger samples.  But the key point remains, it would be absurd to explain replication failures directly as a function of low internal validity.

Construct validity is falsely described as “the degree to which the operationalizations used in the research effectively capture their intended constructs.”  The problem here is the term operationalization. Once a construct is operationalized with some procedure, it is defined by the procedure (intelligence is what the IQ test measures) and there is no way to challenge the validity of the construct. In contrast, measurement implies that constructs exist independent of one specific procedure and it is possible to examine how well a measure reflects variation in the construct (Cronbach & Meehl, 1955).  That said, there is no relationship between construct validity and replicability because systematic measurement error can produce spurious correlations between measures in correlational studies that are highly replicable (e.g., social desirable responding). In experiments, systematic measurement error will attenuate effect sizes, but it will do so equally in original studies and replication studies. Thus, low construct validity also provides no explanation for replication failures.

External validity is defined as “the degree to which an effect generalizes to different populations and contexts”  This validation criterion is also only slightly related to replication failures when there are concerns about contextual sensitivity or hidden moderators. A replication study in a different population or context might fail because the population effect size varies across populations or contexts. While this is possible, there is little evidence that contextual sensitivity is a major factor.

In short, it is a red herring in explanations for replication failures or the replication crisis to talk about validity. Replicability is necessary but not sufficient for good science.

It is therefore not surprising that the authors found most discussions of replication failures focus on statistical conclusion validity. Any other finding would make no sense. It is just not clear why we needed a text analysis to reveal this.

However, the authors seem to be unable to realize that the other types of validity are not related to replication failures when they write “What does this study add? Identifies that statistical conclusion validity is over-emphasized in replication analysis”

Over-emphasized???  This is an absurd conclusion based on a failure to make a clear distinction between replicability/reliability and validity.  

Ulrich Schimmack

Social psychology has an open secret. For decades, social psychologists conducted experiments with low statistical power (i.e., even if the predicted effect is real, their study could not detect it with p < .05), but their journals were filled with significant (p < .05) results. To achieve significant results, social psychologists used so-called questionable research practices that most lay people or undergraduate students consider to be unethical. The consequences of these shady practices became apparent in the past decade when influential results could not be replicated. The famous reproducibility project estimated that only 25% of published significant results are replicable. Most undergraduate students who learn about this fact are shocked and worry about the credibility of results in their social psychology textbooks.

Today, there are two types of social psychologists. Some are actively trying to improve the credibility of social psychology by adopting open science practices such as preregistration of hypothesis, sharing open data, and publishing non-significant results rather than hiding these findings. However, other social psychologists are actively trying to deflect criticism. Unfortunately, it can be difficult for lay people, journalists, or undergraduate students to make sense of articles that make seemingly valid arguments, but only serve the purpose to protect the image of social psychology as a science.

As somebody who has followed the replication crisis in social psychology for the past decade, I can provide some helpful information. In the blog post , I want to point out that Duane T. Wegener and Leandre R. Fabrigar have made numerous false arguments against critics of social psychology, and that their latest article “Evaluating Research in Personality and Social Psychology: Considerations of Statistical Power and Concerns About False Findings” ignores the replication crisis in social psychology and the core problem of selectively publishing significant results from underpowered studies.

The key point of their article is that “statistical power should be de-emphasized in
comparison to current uses in research evaluation” (p. 1105).

To understand why this is a strange recommendation, it is important to understand that power is simply the probability of producing evidence for an effect, when an effect exists. When the criterion for evidence is a p-value below .05, it means the probability of obtaining this desired outcome. One advantage of high power is that researchers get the correct result. In contrast, a study with low power is likely to produce the wrong result called a type-II error. While the study tested a correct hypothesis, the results fail to provide sufficient support for it. As these failures can be due to many reasons (low power or the theory is wrong), they are difficult to interpret and to publish. Often these studies remain unpublished, the published record is biased, and resources were wasted. Thus, high power is a researcher’s friend. To make a comparison, if you could gamble on a slot machine with a 20% chance of winning or an 80% chance of winning, which machine would you pick? The answer is simple. Everybody would rather want to win. The problem is only that researchers have to invest more resources in a single study to increase power. They may not have enough money or time to do so. So, they are more like desperate gamblers. You need a publication, you don’t have enough resources for a well-powered study, so you do a low powered study and hope for the best. Of course, many desperate gamblers lose and are then even more desperate. That is where the analogy ends. Unlike gamblers in a casino, researchers are their own dealers and can use a number of tricks to get the desired outcome (Simmons et al., 2011). Suddenly, a study with only 20% power (chance of winning honestly) can have a chance of winning of 80% or more.

This brings us to the second advantage of high-powered studies. Power determines the outcome of a close replication study. If a researcher conducted a study with 20% power and found some tricks to get significance, the probability of replicating the result honestly is again only 20%. Many unsuspecting graduate students have wasted precious years trying to build on studies that they were not able to replicate. Unless they quickly learned the dark art of obtaining significant results with low power, they did not have a competitive CV to get a job. Thus, selective publishing of underpowered studies is demoralizing and rewards cheating.

None of this is a concern for Wegener and Fabrigar, who do not cite influential articles about the use of questionable research practices (John et al., 2012) or my own work that uses estimates of observed power to reveal those practices (Schimmack, 2012; see also Francis, 2012). Instead, they suggest that “problems with the overuse of power arise when the pre-study concept of power is used retrospectively to evaluate completed research” (p. 1115). The only problem that arises from estimating actual power of completed studies, however, is the detection of questionable practices that produce more reported significant results (often 100%) than one would expect given the low power to do so. Of course, for researchers who want to use QRPs to produce inflated evidence for their theories, this is a a problem However, for consumers of research, the detection of questionable results is desirable so that they can ignore this evidence in favor of honestly reported results based on properly powered studies.

The bulk of Wegener and Fabrigar’s article discusses the relationship between power and the probability of false positive results. A false positive result occurs when a statistically significant result is obtained in the absence of a real effect. The standard criterion of statistical significance, p < .05, states that a researcher that tests 100 false hypothesis without a real effect is expected to obtain 95 non-significant results and 5 false positive results. This may sound sufficient to keep false positive results at a low level. However, the false positive risk is a conditional probability based on a significant result. If a researcher conducts 100 studies, obtains 5 significant results, and interprets these results as real effects, the researcher has a false positive rate of 100% because 5 significant results are expected by chance along. An honest researcher would conclude from a series of studies with only 5 out of 100 significant results that they found no evidence for a real effect.

Now let’s consider a researcher that conducted 100 studies and obtained 24 significant results. As 24 is a lot more than the expected 5 studies by chance along, the researcher can conclude that at least some of the 24 significant results are caused by real effects. However, it is also possible that some of these results are false positives. Soric (1989 – not cited by Wegener and Fabrigar – derived a simple formula to estimate the false discover risk. The formula makes the assumption that studies of real effects have 100% power to detect a real effect. As a result, there are zero studies that fail to provide evidence for a real effect. This assumption makes it possible to estimate the maximum percentage of false positive results.

In this simple example, we have 4 false positive results and 20 studies with evidence for a real effect. Thus, the false positive risk is 4 / 24 = 17%. While 17% is a lot more than 5%, it is still pretty low and doesn’t warrant claims that “most published results are false” (Ioannidis, 2005). Yet, it is also not very reassuring if 17% of published results might be false positives (e.g., 17% of cancer treatments actually do not work). Moreover, based on a single study, we do not know which of the 24 results are true results and false results. With a probability of 17% (1/6), trusting a result is like playing Russian roulette. The solution to this problem is to conduct a replication study. In our example, the 20 true effects will produce significant results again because they were obtained with 100% power to do so. However, the chance to replicate one of the 4 false positive results is only 5/100 * 5 / 100 = 25 / 10,000 = 0.25%. So, with high-powered studies, a single replication study can separate true and false original findings.

Things look different in a world with low powered studies. Let’s assume that studies have only 25% power to produce a significant result, which is in accordance with the success rate in replication studies in social psychology (Open Science Collaboration, 2005).

In this scenario, there is only 1 false positive result and the false positive risk is only 1 out of 21, ~ 5%. Of course, researchers do not know this and have to wonder whether some of 21 significant results are false positives. When they conduct a replication study, only 6 (25/100 * 25/100) of their 20 significant results replicate. Thus, a single replication study does not help to distinguish true and false findings. This leads to confusion and the need for additional studies to separate true and false findings, but low power will produce inconsistent results again and again. The consequences can be seen in the actual literature in social psychology. Many literatures are a selected set of inconsistent results that do not advance theories.

In sum, high powered studies quickly separate true and false findings, whereas low powered studies produce inconsistent results that make it difficult to separate true and false findings (Maxwell, 2004, not cited by Wegener & Fabrigar).

Actions speak louder than Words

Over the past decade, my collaborators and I I have developed powerful statistical tools to estimate the power of studies that were conducted (Bartos & Schimmack, 2021; Brunner & Schimmack, 2022; Schimmack, 2012). In combination with Soric’s (1989) formula, estimates of actual power can also be used to estimate the real false positive risk. Below, I show some results when this method is applied to social psychology. I focus on the journal Personality and Social Psychological Bulletin for two reasons. First, Wegener and Fabrigar were co-editors of this journal right after concerns about questionable research practices and low power became a highly discussed topic and some journal editors changed policies to increase replicability of published results (e.g., Steven Lindsay at Psychological Science). Examining the power of studies published in PSPB when Wegener and Fabrigar were editors provides objective evidence about their actions in response to concerns about replication failures in social psychology. Another reason to focus on PSPB is that Wegener and Fabrigar published their defense of low powered research in this journal, suggesting a favorable attitude towards their position by the current editors. We can therefore examine whether the current editors changed standards or not. Finally, PSPB was edited from 2017 to 2021 by Chris Crandall, who has been a vocal defender of results obtained with questionable research practices on social media.

Let’s start with the years before concerns about replication failures became openly discussed. I focus on the years 2000 to 2012.

Figure 1 shows a z-curve plot of automatically extracted statistical results published in PSPB from 2000 to 2012. All statistical results are converted into z-scores. A z-curve plot is a histogram that shows the distribution of z-scores. One important aspect of a z-curve plot is the percentage of significant results. All z-scores greater than 1.96 (the solid vertical red line) are statistically significant with p < .05 (two-sided). Visual inspection shows a lot more significant results than non-significant results. More precisely, the percentage of significant results (i.e., the Observed Discovery Rate, EDR) is 71%.

Visual inspection of the histogram also shows a strange shape to the distribution of z-scores. While the peak of the distribution is at the point of significance, the shape of the distribution shows a rather steep drop of z-scores just below z = 1.96. Moreover, some of these z-scores are still used to claim support for a hypothesis often called marginally significant. Only z-scores below 1.65 (p < .10, two-sided or .0 5 one-sided, the dotted red line) are usually interpreted as non-significant results. The distribution shows that these results are less likely to be reported. This wonky distribution of z-scores suggests that questionable research practices were used.

Z-curve analysis makes it possible to estimate statistical power based on the distribution of statistically significant results only. Without going into the details of this validated method, the results suggest that the power of studies (i.e., the expected discovery rate, EDR) would only produce 23% significant results. Thus, the actual percentage of 71% significant results is inflated by questionable practices. Moreover, the 23% estimate is consistent with the fact that only 25% of unbiased replication studies produce a significant result (Open Science Collaboration, 2005). With 23% significant results, Soric’s formula yields a false positive risk of 18%. That means, roughly 1 out of 5 published results could be a false positive result.

In sum, while Wegener and Fabrigar do not mention replication failures and questionable research practices, the present results confirm the explanation of replication failures in social psychology as a consequence of using questionable research practices to inflate the success rate of studies with low power (Schimmack, 2020).

Figure 2 shows the z-curve plot for results published during Wegener and Fabrigar’s reign as editors. The results are easily summarized. There is no significant change. Social psychologists continued to publish ~70% significant results with only 20% power to do so. Wegener and Fabrigar might argue that there was not enough time to change practices in response to concerns about questionable practices. However, their 2022 article provides an alternative explanation. They do not consider it a problem when researchers conduct underpowered studies. Rather, the problem is when researchers like me estimate the actual power of studies and reveal that massive use of questionable practices.

The next figure shows the results for Chris Chrandall’s years as editor. While the percentage of significant results remained at 70%, power to produce these results increased to 32%. However, there is uncertainty about this increase and the lower limit of the 95%CI is still only 21%. Even if there was an increase, it would not imply that Chris Crandall caused this increase. A more plausible explanation is that some social psychologists changed their research practices and some of this research was published in PSPB. In other words, Chris Crandall and his editorial team did not discriminate against studies with improved power.

It is too early to evaluate the new editorial team lead by Michael D. Robinson, but for the sake of completeness, I am also posting the results for the last two years. The results show a further increase in power to 48%. Even the lower limit of the confidence interval is now 36%. Thus, even articles published in PSPB are becoming more powerful, much to the dismay of Wegener and Fabrigar, who believe that “the recent overemphasis on statistical
power should be replaced by a broader approach in which statistical and conceptual forms of validity are considered together” (p. 1114). In contrast, I would argue that even an average power of 48% is ridiculously low. An average power of 48% implies that many studies have even less than 48% power.

Conclusion

More than 50 years ago, famous psychologists Amos Tversky and Daniel Kahneman (1971) wrote “we refuse to believe that a serious investigator will knowingly accept a .50 risk of failing
to confirm a valid research hypothesis” (p. 110). Wegener and Fabrigar prove them wrong. Not only are they willing to conduct these studies, they even propose that doing so is scientific and that demanding more power can have many negative side-effects. Similar arguments have been made by other social psychologists (Finkel, Eastwick, Reis, 2017).

I am siding with Kahneman, who realized too late that he placed too much trust in questionable results produced by social psychologists and compared some of this research to a train wreck (Kahneman, 2017). However, there is no consensus among psychologists and readers of social psychological research have to make up their own mind. This blog post only points out that social psychology lacks clear scientific standards and no proper mechanism to ensure that theoretical claims rest on solid empirical foundations. Researchers are still allowed to use questionable research practices to present overly positive results. At this point, the credibility of results depends on researchers’ willingness to embrace open science practices. While many young social psychologists are motivated to do so, Wegener and Fabrigar’s article shows that they are facing resistance from older social psychologists who are trying to defend the status quo of underpowered research.

I am not the first and I will not be the last to point out that the traditional peer-review process is biased. After all, who would take on the thankless job of editing a journal if it would not come with the influence and power to select articles you like and to reject articles you don’t like. Authors can only hope that they find an editor who favors their story during the process of shopping around a paper. This is a long and frustrating process. My friend Rickard Carlsson created a new journal that operates differently with a transparent review process and virtually no rejection rate. Check out Meta-Psychology. I published two articles there that reported results based on math and computer simulations. Nobody challenged the validity, but other journals rejected the work based on politics (AMMPS rejection).

The biggest event in psychology, especially social psychology, in the past decade (2011-2020) was the growing awareness of the damage caused by selective publishing of significant results. It has long been known that psychology journals nearly exclusively publish statistically significant results (Sterling, 1959). This made it impossible to publish studies with non-significant results that could correct false positive results. It was long assumed that this was not a problem because false positive results are rare. What changed over the past decade was that researchers published replication failures that cast doubt on numerous classic findings in social psychology such as unconscious priming or ego-depletion.

Many, if not most, senior social psychologists have responded to the replication crisis in their field with a variety of defense mechanisms, such as repression or denial. Some have responded with intellectualization/rationalization and were able to publish their false arguments to dismiss replication failures in peer-reviewed journals (Bargh, Baumeister, Gilbert, Fiedler, Fiske, Nisbett, Stroebe, Strack, Wilson, etc., to name the most prominent ones). In contrast, critics had a harder time to make their voices heard. Most of my work on this topic has been published in blog posts in part because I don’t have the patience and frustration tolerance to deal with reviewer comments. However, this is not the only reason and in this blog post I want to share what happened when Moritz Heene and I were invited by Christiph Klauer to write an article on this topic for the German journal “Psychological Rundschau”.

For readers who do not know Christipher; he is a very smart social psychologists who worked as an assistant professor with Hubert Feger when I was an undergraduate student. I respect his intelligence and his work such as his work on the Implicit Association Test.

Maybe he invited us to write a commentary because he knew me personally. Maybe he respected what we had to say. In any case, we were invited to write an article and I was motivated to get an easy ‘peer-reviewed’ publication, even if nobody outside of Germany cares about a publication in this journal.

After submitting our manuscript, I received the following response in German.
I used http://www.DeepL.com/Translator (free version) to share an English version.

Thu 2016-04-14 3:50 AM

Dear Uli,

Thank you very much for the interesting and readable manuscript. I enjoyed reading it and can agree with most of the points and arguments. I think this whole debate will be good for psychology (and hopefully social psychology as well), even if some are struggling at the moment. In any case, the awareness of the harmfulness of some previously widespread habits and the realization of the importance of replication has, in my impression, increased significantly among very many colleagues in the last two to three years.

Unfortunately, for formal reasons, the manusrkipt does not fit so well into the planned special issue. As I said, the aim of the special issue is to discuss topics around the replication question in a more fundamental way than is possible in the current discussions and forums, with some distance from the current debates. The article fits very well into the ongoing discussions, with which you and Mr. Heene are explicitly dealing with, but it misses the goal of the special issue. I’m sorry if there was a misunderstanding.

That in itself would not be a reason for rejection, but there is also the fact that a number of people and their contributions to the ongoing debates are critically discussed. According to the tradition of the Psychologische Rundschau, each of them would have to be given the opportunity to respond in the issue. Such a discussion, however, would go far beyond the intended scope of the thematic issue. It would also pose great practical difficulties, because of the German language, to realize this with the English-speaking authors (Ledgerwood; Feldman Barrett; Hewstone, however, I think can speak German; Gilbert). For example, you would have to submit the paper in an English version as well, so that these authors would have a chance to read the criticisms of their statements. Their comments would then have to be translated back into German for the readers of Psychologische Rundschau.

All this, I am afraid, is not feasible within the scope of the special issue in terms of the amount of space and time available. Personally, as I said, I find most of your arguments in the manuscript apt and correct. From experience, however, it is to be expected that the persons criticized will have counter-arguments, and the planned special issue cannot and should not provide such a continuation of the ongoing debates in the Psychologische Rundschau. We currently have too many discussion forums in the Psychologische Rundschau, and I do not want to open yet another one.

I ask for your understanding and apologize once again for apparently not having communicated the objective of the special issue clearly enough. I hope you and Mr. Heene will not hold this against me, even though I realize that you will be disappointed with this decision. However, perhaps the manuscript would fit well in one of the Internet discussion forums on these issues or in a similar setting, of which there are several and which are also emerging all the time. For example, I think the Fachgruppe Allgemeine Psychologie is currently in the process of setting up a new discussion forum on the replicability question (although there was also a deadline at the end of March, but perhaps the person responsible, Ms. Bermeitinger from the University of Hildesheim, is still open for contributions).

I am posting this letter now because the forced resignation of Fiedler as editor of Perspectives on Psychological Science made it salient how political publishing in psychology journals is. While many right-wing media commented on this event to support their anti-woke, pro-doze culture wars. They want to maintain the illusion that current science, I focus on psychology here, is free of ideology and only interested in searching for the truth. This is BS. Psychologists are human beings and show in-group bias. When most psychologists in power are old, White, men, they will favor old, White, men that are like them. Like all systems that work for the people in power, they want to maintain the status quo. Fiedler abused his power to defend the status quo against criticisms of a lack in diversity. He also published several articles to defend (social) psychology against accusations of shoddy practices (questionable research practices).

I am also posting it here because a very smart psychologists stated in private that he agreed with many of our critical comments that we made about replication-crisis deniers. As science is a social game, it is understandable that he never commented on this topic in public (If he doesn’t like that I am making them public, he can say that he was just polite and didn’t really mean what he wrote).

I published a peer-reviewed article on the replication crisis and the shameful response by many social psychologists several years later (Schimmack, 2020). A new generation of social psychologists is trying to correct the mistakes of the previous generation, but as so often, they do so without the support or even against the efforts of the old guard that cannot accept that many of their cherished findings may die with them. But that is life.

Preface

The journal Psychological Inquire publishes theoretical articles that are accompanied by commentaries. In a recent issue, prominent implicit cognition researchers discussed the meaning of the term implicit. This blog post differs from the commentaries by researchers in the field, by providing an outsider perspective and by focusing on the importance of communicating research findings clearly to the general public. This purpose of definitions was largely ignored by researchers who are more focused on communicating with each other than with the general public. I will show that this unique outsider perspective favors a definition of implicit bias in terms of the actual research that has been conducted under the umbrella of implicit social cognition research rather than proposing a definition that renders 30 years of research useless with a simple stroke of a pen. If social cognition researchers want to communicate about implicit bias as empirical scientists they have to define implicit bias as effects of automatically activated information (associations, stereotypes, attitudes) on behavior. This is what they have studied for 30 years. Defining implicit bias as unconscious bias is not helpful because 30 years of research have failed to provide any evidence that people can act in a biased way without awareness. Although unconscious biases may occur, there is currently no scientific evidence to inform the public about unconscious biases. While the existing research on automatically activated stereotypes and attitudes has problems, the topic remains important. As the term implicit bias has caught on, it can be used in communications with the public about, but it should be made clear that implicit does not mean unconscious.

Introduction

Psychologists are notoriously sloppy with language. This leads to misunderstandings and unnecessary conflicts among scientists. However, the bigger problem is a break-down in communication with the general public. This is particularly problematic in social psychology because research on social issues can influence public discourse and ultimately policy decisions.

One of the biggest case-studies of conceptual confusion that had serious real-world consequences is the research on implicit cognition that created the popular concept of implicit bias. Although the term implicit bias is widely used to talk about racism, the term lacks clear meaning.

The Stanford Encyclopedia of Philosophy defines implicit bias as a tendency to “act on the basis of prejudice and stereotypes without intending to do so.” However, lack of intention (not wanting to) is only one of several meanings of the term implicit. Another meaning of the word implicit is automatic activation of thoughts. For example, a Scientific American article describes implicit bias as a “tendency for stereotype-confirming thoughts to pass spontaneously through our minds.” Notably, this definition of implicit bias clearly implies that people are aware of the activated stereotype. The stereotype-confirming thought is in people’s mind and not activated in some other area of the brain that is not accessible to consciousness. This definition also does not imply that implicit bias results in biased behavior because awareness makes it possible to control the influence of activated stereotypes on behavior.

Merriam Webster Dictionary offers another definition of implicit bias as “a bias or prejudice that is present but not consciously held or recognized.” In contrast to the first two meanings of implicit bias, this definition suggests that implicit bias may occur without awareness; that is implicit bias = unconscious bias.

The different definitions of implicit bias lead to very different explanations of biased behavior. One explanation assumes that implicit biases can be activated and guide behavior without awareness and individuals who act in a biased way may either fail to recognize their biases or make up some false explanation for their biased behaviors after the fact. This idea is akin to Freud’s notion of a powerful, autonomous unconscious (the Id) that can have subversive effects on behavior that contradict the values of a conscious, moral self (Super-Ego). Given the persistent influence of Freud on contemporary culture, this idea of implicit bias is popular and reinforced by the Project Implicit website that offers visitors tests to explore their hidden (hidden = unconscious) biases.

The alternative interpretation of implicit bias is less mysterious and more mundane. It means that our brain constantly retrieves information from memory that is related to the situation we are in. This process does not have a filter to retrieve only information that we want. As a result, we sometimes have unwanted thoughts. For example, even individuals who do not want to be prejudice will sometimes have unwanted stereotypes and associated negative feelings pop into their mind (Scientific American). No psychoanalysis or implicit test is needed to notice that our memory has stored stereotypes. In safe contexts, we may even laugh about them (Family Guy). In theory, awareness that a stereotype was activated also makes it possible to make sure that it does not influence behavior. This may even be the main reason for our ability to notice what our brain is doing. Rather than acting in a reflexive way to a situation, awareness makes it possible to respond more flexible to a situation. When implicit is defined as automatic activation of a thought, the distinction between implicit and explicit bias becomes minor and academic because the processes that retrieve information information from memory are automatic. The only difference between implicit and explicit retrieval of information is that the process may be triggered spontaneously by something in our environment or by a deliberate search for information.

After more than 30 years of research on implicit cognitions (Fazio, Sanbonmatsu, Powell, Kardes, 1986), implicit social cognition researchers increasingly recognize the need for clearer definitions of the term implicit (Gawronski, Ledgerwood, & Eastwick, 20222a), but there is little evidence that they can agree on a definition (Gawronski, Ledgerwood, & Eastwick, 20222b). Gawronski et al. (2022a, 2022b) propose to limit the meaning of implicit bias to unconscious biases; that is, individuals are unaware that their behavior was influenced by activation of negative stereotypes or affects/attitudes. “instances of bias can be described as implicit if respondents are unaware of the effect of social category cues on their behavioral response” (p. 140). I argue that this definition is problematic because there is no scientific evidence to support the hypothesis that prejudice is unconscious. Thus, the term cannot be used to communicate scientific results that have been obtained by implicit cognition researchers over the past three decades because these studies did not study unconscious bias.

Implicit Bias Is Not Unconscious Bias

Gawronski et al. note that their decision to limit the term implicit to mean unconscious is arbitrary. “A potential objection against our arguments might be that they are based on a particular interpretation of implicit in IB that treats the term as synonymous with unconscious” (p. 145). Gawronski et al. argue in favor of their definition because “unconscious biases have the potential to cause social harm in ways that are fundamentally different from conscious biases that are unintentional and hard-to-control” (p. 146). The key words in this argument is “have the potential,” which means that there is no scientific evidence that shows different effects of biases with and without awareness of bias. Thus, the distinction is merely a theoretical, academic one without actual real-world implications. Gawronski et al. agree with this assessment when they point out that existing implicit cognition research “provides no information about IB [implicit bias] if IB is understood as an unconscious effect of social category cues on behavioral responses. It seems bizarre to define the term implicit bias in a way that makes all of the existing implicit cognition research irrelevant. A more reasonable approach would be to define implicit bias in a way that is more consistent with the work of implicit bias researchers. As several commentators pointed out, the most widely used meaning of implicit is automatic activation of information stored in memory about social groups. In fact, Gawronski himself used the term implicit in this sense and repeatedly pointed out that implicit does not mean unconscious (i.e., without awareness) (Appendix 1).

Defining the term implicit as automatic activation makes sense because the standard experimental procedure to study implicit cognition is based on presenting stimuli (words, faces, names) related to a specific group and to examine how these stimuli influence behaviors such as the speed of pressing a button on a keyboard. The activation of stereotypic information is automatic because participants are not told to attend to these stimuli or even to ignore them. Sometimes the stimuli are also presented in subtle ways to make it less likely that participants consciously attend to them. The question is always whether these stimuli activate stereotypes and attitudes stored in memory and how activation of this information influences behavior. If behavior is influenced by the stimuli, it suggests that stereotypic information was activated – with or without awareness. The evidence from studies like these provides the scientific basis for claims about implicit bias. Thus, implicit bias is basically operationally defined as systematic effects of automatically activated information about groups on behavior.

The aim of implicit bias research is to study real-word incidences of prejudice under controlled laboratory conditions. A recent incidence at racism shows how activation of stereotypes can have harmful consequences for victims and perpetrators of racist behavior .

University of Kentucky student who repeatedly hurled racist slur at Black student permanently banned from campus

The question of consciousness is secondary. What is important is how individuals can prevent harmful consequences of prejudice. What can individuals do to avoid storing negative stereotypes and attitudes in the first place? What can individuals do to weaken stored memories and attitudes? What can individuals do to make it less likely that stereotypes are activated? What can individuals do to control the influence of attitudes when they are activated? All of these questions are important and are related to the concept of implicit as automatic activation of attitudes. The only reason to emphasize unconscious process would be a scenario where individuals are unable to control the influence of information that influences behavior without awareness. However, given the lack of evidence that unconscious biases exist, it is currently unnecessary to focus on this scenario. Clearly, many instances of biases occur with awareness (“White teacher in Texas fired after telling students his race is ‘the superior one’”).

Unfortunately, it may be surprising for some readers to learn that implicit does not mean unconscious because the term implicit bias has been popularized in part to make a distinction between well-known forms of bias and prejudice and a new form of bias that can influence behavior even when individuals are consciously trying to be unbiased. These hidden biases occur against individuals’ best intentions because they exist in a blind spot of consciousness. This meaning of implicit bias was popularized by Banaji and Greenwald (2013), who also founded the Project Implicit website that provides individuals with feedback about their hidden biases; akin to psychoanalysts who can recover repressed memories.

Gawronski et al. (2022b) point out that Greenwald and Banaji’s theory of unconscious bias evolved independently of research by other implicit bias researchers who focused on automaticity and were less concerned about the distinction between conscious and unconscious biases. Gawronski’s definition of implicit bias as unconscious bias favors Banaji and Greenwald’s school of thought (hidden bias) over other research programs (automatically activated biases). The problem with this decision is that Greenwald and Banaji recently walked back their claims about unconscious biases and no longer maintain that the effects they studies were obtained without awareness (Implicit = Indirect & Indirect ≠ Unconscious, Greenwald & Banaji, 2017). The reversal of their theoretical position is evident in their statement that “even though the present authors find themselves occasionally lapsing to use implicit and explicit as if they had conceptual meaning [unconscious vs. conscious], they strongly endorse the empirical understanding of the implicit– explicit distinction” (p. 892). It is puzzling to see Gawronski arguing for a definition that is based on a theory that the authors no longer endorse. Given the lack of scientific evidence that stereotypes regularly lead to biases without awareness, this might be the time to agree on a definition that matches the actual research by implicit cognition researchers, and the most fitting definition would be automatic activation of stereotypes and attitudes, not unconscious causes of behavior.

Gawronski et al. (2022a) also falsely imply that implicit cognition researchers have ignored the distinction between conscious and unconscious biases. In reality, numerous studies have tried to demonstrate that implicit biases can occur without awareness. To study unconscious biases, social cognition researchers have relied heavily on an experimental procedure known as subliminal priming. In a subliminal priming study, a stimulus (prime) is presented very briefly, outside of the focus of attention, and/or with a masking stimuli. If a manipulation check shows that individuals have no awareness of the prime and the prime influences behavior, the effect appears to occur without awareness. Several studies suggested that racial primes can influence behavior without awareness (Bargh et al., 1996; Davis, 1989).

However, the credibility of these results has been demolished by the replication crisis in social psychology (Open Science Collaboration, 2015; Schimmack, 2020). Priming research has been singled out as the field with the biggest replication problems (Kahneman, 2012). When asked to replicate their own findings, leading priming researchers like Bargh refused to do so. Thus, while subliminal priming studies started the implicit revolution (Greenwald & Banaji, 2017), the revolution imploded over the past decade when doubts about the credibility of the original findings increased.

Unfortunately, researchers within the field of implicit bias research often ignore the replication crisis and cite questionable evidence as if it provided solid evidence for unconscious biases. For example, Gawronski et al. (2022b) suggest that unconscious biases may contribute to racial disparities in use-of-force errors such as the high-profile killing of Philando Castile. To make this case, they use a (single) study of 58 White undergraduate students (Correll, Wittenbrink, Crawford, & Sadler, 2015, Study 3). The study asked participants to make shoot vs. no-shoot decisions in a computer task (game) that presented pictures of White or Black men holding a gun or another object. Participants were instructed to make one quick decision within 630 milliseconds and another decision without time restriction. Gawronski et al. suggest that failures to correct an impulsive error given ample time to do so constitutes evidence of unconscious bias. They summarized the results as evidence that “unconscious effects on basic perceptual processes play a major role in tasks that more closely resemble real-world settings” (p. 226).

Fact checking reveals that this characterization of the study and its results is at least misleading, if not outright false. First, it is important to realize that the critical picture was presented for only 175ms and immediately replaced by another picture to wipe out visual memory. Although this is not a strictly subliminal presentation of stimuli, it is clearly a suboptimal presentation of stimuli. As a result, participants sometimes had to guess what the object was. They also had no other information to know whether their initial perception was correct or incorrect. The fact that participants’ performance improved without time pressure may be due to response errors under time pressure and this improvement was evident independent of the race of the men in the picture.

Without time pressure, participants shot 85% of armed Black men and 83% of armed White men. For unarmed men, participants shot 28% Black men and 25% White men. The statistical comparison of these differences showed weak effect of a systematic bias. The comparison for unarmed men produced a p-value that was just significant with the standard criterion of alpha = .05 criterion, F(1,53) = 6.65, p = .013, but not the more stringent criterion of alpha = .005 that is used to predict a high chance of replication. The same is true for the comparison of responses to pictures of unarmed men, F(1,53) = 4.96, p =.031. To my knowledge, this study has not been replicated and Gawronski et al.’s claim rests entirely on this single study.

Even if these effects could be replicated in the laboratory, they do not provide any information about unconscious biases in the real world because the study lacks ecological validity. To make claims about the real world, it is necessary to study police officers in simulations of real world scenarios (Andersen, Di Nota, Boychuk, Schimmack, & Collins, 2021). This research is rare, difficult, and has not yet produced conclusive results. Andersen et al. (2021) found a small racial bias, but the sample was too small to provide meaningful information about the amount of racial bias in the real world. Most important, however, real-word scenarios provide ample information to see whether a suspect is Black or White and is armed or not. The real decision is often whether use of force is warranted or not. Racial biases in these shooting errors are important, but they are not unconscious biases.

Contrary to Gawronski et al., I do not believe that social cognition researchers focus on automatic biases rather than unconscious biases was a mistake. The real mistake was the focus on reaction times in artificial computer tasks rather than studying racial biases in the real world. As a result, thirty years of research on automatic biases has produced little insights into racial biases in the real world. To move the field towards the study of unconscious biases would be a mistake. Instead, social cognition researchers need to focus on outcome variables that matter.

Conclusion

The term implicit bias can have different meanings. Gawronski et al. (2022a) proposed to limit the meaning of the term to unconscious bias. I argue that this definition of implicit bias is not useful because most studies of implicit cognition are studies in which racial stereotypes and attitudes toward stigmatized groups are automatically activated. In contrast, priming studies that tried to distinguish between conscious and unconscious activation of this information have been discredited during the replication crisis and there exists no credible empirical evidence to suggest that unconscious biases exist or contribute to real-world behavior. Thus, funding a new research agenda focusing on unconscious biases may waste resources that are better spent on real-world studies of racial biases. Evidently, this conclusion diverges from the conclusion of implicit cognition researchers who are interested in continuing their laboratory studies, but they have failed to demonstrate that their work makes a meaningful contribution to society. To make research on automatic biases more meaningful, implicit bias research needs to move from artificial outcomes like reaction times on computer tasks to actual behaviors.

Appendix 1

Implicit Cognition Research Focusses on Automatic (Not Unconscious) Processes

Gawronski & Bodenhausen (2006), WOS/11/22 1,537

“If eras of psychological research can be characterized in terms of general ideas, a major theme of the current era is probably the notion of automaticity” (p. 692)

This perspective is also dominant in contemporary research on attitudes, in which deliberate, “explicit” attitudes are often contrasted with automatic, “implicit” attitudes (Greenwald & Banaji, 1995; Petty, Fazio, & Brin˜ol, in press; Wilson, Lindsey, &
Schooler, 2000; Wittenbrink & Schwarz, in press).

“We assume that people generally do have some degree of conscious access to their automatic affective reactions and that they tend to rely on these affective reactions in making evaluative judgments (Gawronski, Hofmann, & Wilbur, in press; Schimmack & Crites, 2005) (p. 696).

Conrey, Sherman, Gawronski, Hugenberg, & Groom (2005) , WOS/11/22

“The distinction between automatic and controlled processes now occupies a central role in many areas of social psychology and is reflected in contemporary dual-process theories of prejudice and stereotyping (e.g., Devine, 1989)” (p. 469)

“Specifically, we argued that performance on implicit measures is influenced by at least four different processes: the automatic activation of an association (association activation), the ability to determine a correct response (discriminability), the success at overcoming automatically activated associations (overcoming bias), and the influence of response biases
that may influence responses in the absence of other available guides to response (guessing)” (p. 482)

Gawronski & DeHouwer (2014), WOS 11/22 240

” other researchers assume that the two kinds of 11lL’asurcs tap into distinct memory representations, such that explicit measures tap into conscious representations whereas implicit measures tap into unconscious representations (e.g., Greenwald &
Banaji, 1995). Although the conceptualizations arc relatively common in the literature on implicit measures, we believe that it is concecptually more appropriate to classify different measures in terms of whether the tobe-measured psychological attribute influences participants’ responses on the task in an automatic fashion (De Houwer, Teige-Mocigemba, Spruyt, & Moors, 2009).” (p. 283)

Hofmann, Gawronski, Le, & Schmitt, PSPB, 2005, WoS/11/22

“These [implicit] measures—most of them based on reaction times in response compatibility tasks (cf. De Houwer, 2003)—are intended to assess relatively automatic mental associations that are difficult to gauge with explicit self-report measures”. (p. 1369)

Gawronski, Hofmann, & Wilbur (2006), WoS/11/22 200

“A common explanation for these findings is that the spontaneous behavior assessed in these
studies is difficult to control, and thus more likely to be influenced by automatic evaluations, such as they are reflected in indirect attitude measures” (p. 492)

“there is no empirical evidence that people lack conscious awareness of indirectly assessed attitudes per se” (p. 496)

Gawronski, LeBel, & Peters, PoPS (2007) WOS/11/22 187

“The central assumption in this model is that indirect measures provide a proxy for the activation of associations in memory” (p. 187)

Gawronski & LeBel, JESP (2008) WOS/11/22

“We argue that implicit measures provide a proxy for automatic associations in memory,
which may or may not influence verbal judgments reflected in self-report measures” (p. 1356)

Deutsch, Gawronski, & Strack, JPSP (2006), WOS/11/22 122

“Phenomena such as stereotype and attitude activation can be readily reconstructed as instance-based automaticity. For example, perceiving a person of a stereotyped group or an
attitude object may be sufficient to activate well-practiced stereotypic or evaluative associations in memory” (p. 386)

Implicit measures are important even if they do not assess unconscious processes.

Hofmann, Gawronski, Le, & Schmitt, PSPB, 2005, WoS/11/22

” Arguably one of the most important contributions in social cognition research within the last decade was the development of implicit measures of attitudes, stereotypes, self-concept, and self-esteem (e.g., Fazio, Jackson, Dunton, & Williams, 1995; Greenwald, McGhee, & Schwartz, 1998; Nosek & Banaji, 2001; Wittenbrink, Judd, & Park, 1997).” (p. 1369)

Gawronski & DeHouwer (2014), WOS 11/22 240

“For the decade to come, we believe that the field would benefit from a stronger focus on underlying mechanisms with regard to the measures themselves as well as their capability to predict behavior (see also Nosek, Hawkins, & Frazier, 2011).” (p. 303)

Post-war American Psychology is rooted in behaviorism. The key assumption of behaviorism is that psychology (i.e., the science of the mind) should only study phenomena that are directly observable. As a result, the science of the mind became the science of behavior. While behaviorism is long dead (see the 1990 funeral here), it’s (harmful) effect on psychology is still noticeable today. One lasting effect is psychologists aversion to make causal attributions to the mind (cognitive processes). While cognitive processes cannot be directly observed with the human senses (we cannot see, touch, smell, or hear what goes on in somebody’s mind), we can indirectly observe these processes on the basis of observable behaviors. A whole different discipline that is called psychometrics has developed elaborate theories and statistical models to relate observed behaviors to unobserved processes in the mind. Unfortunately, psychometrics is often not covered in the education of psychologists. As a result, psychologists often make simple mistakes when they apply psychometric tools to psychological questions.

In the language of psychometrics, observed behaviors are observed variables and unobserved mental processes are unobserved variables that are also often called latent (i.e., of a quality or state) existing but not yet developed or manifest; hidden or concealed) variables. The goal of psychometrics is to find systematic relationships between observed and latent variables that make it possible to study mental processes. We can compare this process to the task of early astronomers to make sense of the lights in the night sky. Bright stars are like observable indicators and the task of astronomers is to explain the behavior of these observable variables with unobserved forces. Astronomy has come a long way from seeing astrological signs in the sky, but psychology is pretty much at this early stage of science, where most of the unknown cognitive processes that cause observable behaviors are unknown. In fact, some psychologists still resist the idea that observable behavior can be explained by latent variables (Borsboom et al., 2021). Others, however, have used psychometric tools, but fail to understand the basic properties of psychometric models (e.g., Digman, 1997; DeYoung & Peterson, 2002; Musek, 2007). Here, I give a simple introduction to the basic logic of psychometric models and illustrate how applied psychologists can get lost in latent variable space.

Figure 2 shows the most basic psychometric model that relates an observed variable to an unobserved cause. I am using a widely used measure of life-satisfaction as an example. Please rate your life on a scale from 0 = worst possible life to 10 = best possible life. Thousands of studies with millions of respondents have used this question to study “the secret of happiness.” Behaviorists would treat this item as a stimulus and participants responses on the 11-point rating scales as behaviors. One problem for behaviorists is that participants will respond differently to the same question. Responses vary from 0 (very rarely) all the way to 10 (more often, but still rare). The modal response in affluent Western countries is 7. Behaviorism has no answer to the question why participants respond differently to the same situation (i.e., question). Some researchers have tried to provide a behavioristic answers by demonstrating that responses can be manipulated (e.g., responses are different in a good or bad mood; Schwarz & Strack, 1999; Kahneman, 2011). However, these effects are small and do not explain why responses are highly stable over time and across different situations (Schimmack & Oishi, 2005). To explain why some people report higher levels of life-satisfaction than others, we have to invoke unobserved causes within respondents’ minds. Just like forces that creates the universe, these causes are not directly observable, but we know they must exist because we observe variation in responses that cannot be explained by variation in the situation (i.e., same situation and different behaviors imply internal causes).

Psychologists have tried to understand the mental processes that produce variation in Cantril ladder scores for nearly 100 years (Andrews & Whitey, 1976; Cantril, 1965; Diener, 1984; Hartmann, 1936). In the 1980s, focus shifted from thoughts about one’s life (e.g., I hate my work, I love my spouse, etc.) to the influence of personality traits (Costa & McCrae, 1980). Just like life-satisfaction, personality is a latent variable that can only be measured indirectly by observing differences in behaviors in the same situation. The most widely used observed variables to do so are self-ratings of personality.

The key problem for the measurement of unobserved mental processes is that variation in observed scores can be caused by many different mental processes. To go beyond the level of observed variation in behaviors, it is necessary to separate the different causes that contribute to the variance in observed scores. The first step is to separate causes that produce measurement error. The most widely used approach to do so is to ask the same or similar questions repeatedly and to consider variability in responses as measurement error. The next figure shows a model for responses to two similar items.

When two or more observed variables are available, it is possible to examine the correlation between two variables. if two observed variables share a common cause, they are going to be correlated. The strength of the correlation depends on the relative strength of the shared mental process and the unique mental processes. Psychometrics works in reverse and makes inferences about the unobserved causes by examining the observed correlations. To do so, it is necessary to make some assumptions, and this is where things can go wrong, when researchers do not understand these assumptions.

A common assumption is that the shared causal processes are important and meaningful, whereas the unique mental processes are unimportant, irrelevant, and error variance. Based on this assumption, the model is often drawn differently. Sometimes, the shared unobserved variable is drawn on top, and the unshared unobserved variables are drawn at the bottom (top = important, bottom = unimportant).

Sometimes, the unique mental processes are drawn smaller and without a name.

And sometimes, they are simply omitted because they are considered unimportant and irrelevant.

The omission of the unshared causes makes sense when psychometricians communicate with each other because they are trained in understanding psychometric models and use figures merely as a short-hand to communicate with each other. However, when psychometricians communicate with psychologists things can go horribly wrong because psychologists may not realize that the omission of residuals is based on assumptions that can be right or wrong. They may simply assume that the unique variances are never important and can always be omitted. However, this is a big mistake with undesirable consequences. To demonstrate this, I am always going to show the unique causes of all variables in the following models.

When psychologists ask similar questions repeatedly, they are assuming that the unique causes of the responses are measurement error. In the present example, individuals may interpret the words “worry” and “nervous” somewhat differently and this may elicit different mental processes that result in slightly different responses. However, the two terms are sufficiently similar that they also elicit similar cognitive processes that produce a correlation between responses to the two items. Under this assumption, the common causes reflect the causes that are of interest and the unique causes produce error variance. Under the assumption that unique causes produce error variance, it is possible to average responses to similar items. These averages are called scales. Averaging amplifies the variance that is produced by shared causes.

This is illustrated in the next figure where the average is fully determined by the two observed variables “I often worry” and “I am often nervous.” To make this a measurement model, we have to relate the average scores to the unobserved variables. Now we see that the shared mental process variable has two ways to influence the average scores, whereas each of the unique causes has only one way to contribute to the average. As the number of variables increases the ratio (2:1) becomes even bigger for the shared variable (3 variables, 3:1). This implies that the shared mental processes more and more determine the average scores. This is the only part of measurement theory that psychologists are taught and understand as reflected in the common practice to report Cronbach’s alpha (a measure of the shared variance in the average scored) as evidence that a measure is a good measure (Flake & Fried, 2020). However, the real measurement problems are not addressed by averaging across similarly-worded items. This is revealed in the next figure.

To use the average of responses to similarly worded items as an observed measure of an unobserved personality trait, we have to assume that the shared mental processes that produce most of the variance in the average scores are caused by the personality trait that we are trying to measure. In the present example, personality psychologists use items like “worry” and “nervous” to measure a trait called Neuroticism. Despite 100 years of research, it is still not clear what Neuroticism is and some psychologists still doubt that Neuroticism even exists. Those who do believe in Neuroticism assume it reflects a general disposition to have more negative thoughts (e.g., low self-esteem, pessimism) and feelings (anxiety, anger, sadness, guilt). The main problem in current personality research is that item-averages are often treated as if they are perfect observed indicators of an unobserved personality trait (see next figure).

Ample research suggests that average scores of neuroticism items are also influenced by other factors such as socially desirable responding. Thus, it is a simplification to assume that item-averages are identical or isomorphous to the personality trait that they are designed to measure. Nevertheless, it is common for personality psychologists to study the influence of unobserved causes like Neuroticism by means of item averages. As we see later, even when psychologists use latent variable models, Neuroticism is just a label for an item-average. The problem with this practice is that it gives the illusion that we can study the causal effects of unobservable personality traits by examining the correlations of observable item-averages.

In this way, measurement problems are treated as unimportant, just like behaviorists considered mental processes as unimportant and relegated them to a black box that should not be examined. The same attitude prevails today with regards to personality measurement, when boxes (observed variables) are given names without checking that the labels actually match the content of the box (i.e., the unobserved causes that a measure is supposed to reflect). Often psychological constructs are merely labels for item-averages. Accordingly, neuroticism is ‘operationalized’ with an item-average and neuroticism can be defined as “whatever a neuroticism scale measures.”

When Things Go from Bad to Worse

In the 1980s, personality psychologists came to a broad consensus that the diversity of human traits (e.g., anxious, bold, curious, determined, energetic, frank, gentle, helpful, etc.) can be organized into a taxonomy with five broad traits, known as the Big Five. The basic idea is illustrate in the next Figure with Neuroticism. According to Big Five theory, Neuroticism is a general disposition to experience more anxiety, anger, and sadness. However, each emotion also has its one dispositions. Thus, variation in scales that measure anxiety, anger, and sadness is influenced by both Neuroticism (i.e., the general disposition) and specific causes. In addition, scales can also be influenced by general and specific measurement errors. The figure makes it clear that the scores in the item-averages can reflect many different causes aside from the intended broader personality trait called Neuroticism. This makes it risky to rely on these item averages to draw inferences about the unobserved variable Neuroticism.

A true science of personality would try to separate these different causes and to examine how they relate to other variables. However, personality psychologists often hide the complexity of personality measurement by treating personality scales as if they directly reflect a single cause). While this is bad enough, things get even worse when personality psychologists speculate about even broader personality traits.

The General Personality Factor (Musek, 2007)

The Big Five were considered to be roughly independent from each other. In fact, they were found with a method that looked for independent factors (another name for unobserved variables) more commonly used in personality research. However, when Digman (1997) examined correlations among item-averages, he found some systematic patterns in these correlations. This led him to postulate even broader factors than the Big Five that might explain these patterns. The problem with these theories is that they are no longer trying to relate observed variables to unobserved variables. Rather, Digman started to speculate about causal relationships among unobserved variables on the basis of imperfect indicators of the Big Five.

The first problem with Digman’s attempt to explain correlations among unobserved variables was that he lacked expertise in the use of psychometric models. As a result, he made some mistakes and his results could not be replicated (Anusic et al., 2009). A few years later, a study that controlled for some of the measurement problems by using self-ratings and informant ratings suggested that the Big Five are more or less independent and that correlations reflect measurement error (Biesanz & West, 2004; see also Anusic et al., 2009). However, other studies suggested that higher-order factors exists and may have powerful effects on people’s lives, including their well-being. Subsequently, I am going to show that these claims are based on a simple misunderstanding of measurement models that treat unique variance in the Big Five scales as error variance.

Musek (2007) proposed that correlations among Big Five scales can be explained with a single higher-order factor. This model is illustrated in his Figure 1.

First, it is notable that the unique mental processes that contribute to each of the Big Five scales are called e1 to e5 and the legend of the figure explains that e stands for error variances. This terminology can be justified if we treat Big Five scales only as observed variables that help us to observe the unobserved variable GFP. As GFP is not directly observable, we have to infer its presence from the correlations among the observed variables, namely the Big Five scales. However, labeling the unique causes that produce variation in Neuroticism scores error variance is dangerous because we may think that the unique variance in Neuroticism is no longer important; just error. Of course, this variance is not error variance in some absolute sense. After all, Neuroticism scales exists only because personality psychologists assume that Neuroticism is a real personality trait that is related to even more specific traits like anxiety, anger, and sadness. Thus, all of the variance in a neuroticism scale is assumed to be important and it would be wrong to assume that only the variance shared with other Big Five scales is important. To avoid this misinterpretation, it would be better to keep the unique causes in the model.

Another problem of this model is that the model itself provides no information about the actual causes of the correlations among the Big Five scales. This is different when items are written for the explicit purpose of measuring something that they have in common. In contrast, the correlations among the Big Five traits are an empirical phenomenon that requires further investigation to understand the nature of the causal processes that produce correlations. In other words, GFP is just a name for “shared cognitive processes;” it does not tell us what these shared cognitive processes are. To examine this question, it is necessary to see how the GFP is related to other things. This is where things go horribly wrong. Rather than relating the unobserved variable in Figure 1 to other measures, Musek (2007) averages all Big Five items to create an item average that is supposed to represent the unobserved variable. He then uses correlations of the GFP scale to make inferences about the GFP factor. The problems of this approach are illustrated with the next figure.

The figure illustrates that the general personality scale is not a good indicator of the general personality factor. The main problem is that the scale scores are also influenced by the unique causes that contribute to variation in the Big Five scales (on top of measurement error that is not shown in the picture to avoid clutter, but should not be forgotten). The problem is hidden when the unique causes are represented as errors, but unique variance in neuroticism is not error variance. It reflects a disposition to have more negative thoughts and this disposition could have a negative influence on life-satisfaction. This contribution of unique causes is hidden when Big Fife scale scores are averaged and labeled General Personality.

Musek (2007) reports a correlation of r = .5 (Study 1) between the general personality scale and a life-satisfaction scale. Musek claims that this high correlation must reveal a true relationship between the general factor of personality and life-satisfaction and cannot reflect a method artifact like social desirable responding. It is unclear why Musek (2007) relied on an average of Big Five scale scores to examine the relationship of the general factor with life-satisfaction. Latent variable modeling makes it possible to examine the relationship of the general factor directly without the need for scale scores. Fortunately, it is possible to conduct this analysis post-hoc based on the reported correlations in Table 1.

The first model created a general personality scale and used the scale as a predictor of life-satisfaction. The only difference to a simple correlation is that the model also includes the implied measurement model. This makes the model testable because it imposes restrictions on the correlations of the Big Five scales with the life-satisfaction scale. The fit of the model was acceptable, but not great, suggesting that alternative models might produce even better fit, RMSEA = .078, CFI = .958.

In this model, it is possible to trace the paths from the unobserved variables to life-satisfaction. The strongest relationship was the path from the general personality factor (h) to life-satisfaction, b = .42, se = .04, but the model also implied that unique variances of the Big Five scales contribute to life-satisfaction. These effects are hidden when the general personality scale is interpreted as if it is a pure measure of the general personality factor.

A direct test of the assumption that the general factor is the only predictor of life-satisfaction requires a simple modification of the model that links life-satisfaction directly to the general factor (h). This model actually fits the data better, RMSEA = .048, CFI = .984. This might suggest that the unique causes of variation in the Big Five are unrelated to life-satisfaction.

However, good fit is not sufficient to accept a model. It is also important to rule out plausible alternative models. An alternative model assumes that the Big Five factors are necessary and sufficient to explain variation in life-satisfaction. There is no reason to create a general scale and use it as a predictor. Instead, life-satisfaction can simply be regressed onto the Big Five scales as indicator of the Big Five factors. In fact, it is always possible to get good fit for a model that uses indicators as predictors of outcomes because the model does not impose any restrictions (i.e., the model is just identified). The only reason why this model fits worse than the other model is that fit indices like RMSEA and CFI reward parsimony and this model uses 5 predictors of life-satisfaction whereas the previous model had only one predictor. However, parsimony cannot be used to falsify a model.

In fact, it is possible to find an even better fitting model because only two of the five Big Five scales were significant predictors of life-satisfaction. This finding is consistent with many previous studies that these two Big Five traits are the strongest predictors of life-satisfaction. If the model is limited to these two predictors, it fits the data better than the model with a direct path from the general factor, CFI = .987, RMSEA = .045. Musek (2007) was unable to realize that the unique variances in neuroticism and extraversion make a unique contribution to life-satisfaction because the general personality scale does not separate shared and unique causes of variation in the Big Five scales.

The Correlated Big Two

In contrast to Musek (2007), DeYoung and Peterson favor a model with two correlated higher-order factors (DeYoung, Peterson, & Higgins, 2002; see Schimmack, 2022, for a detailed discussion).

As Musek (2007) they treat the unique causes of variation in Big Five traits as error (e1-e5) and assume that relationships of the higher-order factors with criterion variables are direct rather than being mediated by the Big Five factors. Here, I fitted this model to Musek’s (2007) data. Fit was excellent, CFI = .996, RMSEA = .030.

Based on this model, life-satisfaction would be mostly predicted by stability rather than neuroticism and extraversion or a general factor. However, just because this model has excellent fit doesn’t mean it is the best model. The model simply masks the presence of a general factor by modeling the shared variance between Plasticity and Stability as a correlated residual. It is also possible to model it with a general factor. In this model, Stability and Plasticity would be an additional level in a hierarchy between the Big Five and the General Factor. This model does not impose any additional restrictions and fits the data as well as the previous model, CFI = .996, RMSEA = .030. Thus, even though Stability and Plasticity can be identified, it does not mean that this distinction is important for the prediction of life-satisfaction. The general factor could still be the key predictor of life-satisfaction.

However, both models make the assumption that the unique causes of variation in Big Five scales are unrelated to life-satisfaction, and we already saw that this assumption is false. As a result, the model that relates life-satisfaction to neuroticism and extraversion fits the data, CFI = .994, RMSEA = .035, and the paths from extraversion and neuroticism to life-satisfaction were significant.

Musek (2007) and DeYoung et al. (2006) ignored the possibility that unique causes of variation in the Big Five contribute to the prediction of other variables because they made the mistake to equate unique variances with error variances. This interpretation is based on the basic examples that are used to illustrate latent variable models for beginners. However, the interpretation of all aspects of a latent variable model, including the residual or unique variances has to be guided by theory. To avoid these mistakes, psychometricians need to stop presenting their models as if they can be used without substantive theory and substantive researchers need to get better training in the use of psychometric tools.

Conclusion

Compared to other sciences like physics, astronomy, chemistry, or biology, psychology has made little progress over the past 40 years. While there are many reasons for this lack of progress, one problem is the legacy of behaviorism to focus on observable behaviors and to rely on experimentation as the only scientific approach to test causal theories. Another problem is an ideological bias against personality as a causal force that produces variation between individuals (Mischel, 1968). To make progress, personality science has to adopt a new scientific approach that uses observed behaviors to test causal theories of unobservable forces like personality. While personality scales can be used to predict behaviors and life-outcomes, they cannot explain behaviors and life-outcomes. Latent variable modeling provides a powerful tool to test causal theories. The biggest advantage of latent variable modeling is that model fit can be used to reject models. A cynic might think that this is the main reason why they are ot used more by psychologists because it is more fun to build a theory and confirm it rather than to find out that it was false, but fun doesn’t equal scientific progress.

P.S. What about Network Models?

Of course, it is also possible to reject the idea of unobserved variables altogether and draw pictures of the correlations (or partial correlations) among all the observed variables. The advantage of this approach is that it always produces results that can be used to tell an interesting story about the data. The disadvantage is that it always produces a result and therefore doesn’t test any theory. Thus, these models cannot be used to advance personality psychology towards a science that progresses by testing and rejecting false theories.