Abstract

An influential model of personality disorders assumes a general factor of personality functioning that underlies the presence of personality disorder symptoms. To measure this factor, Morey (2017) developed the Level of Personality Functioning scale. The construct and the measure of general personality functioning, however, remains controversial. Here I analyze data that were used to claim validity of the LPFS using structural equation modeling. I demonstrate that two factors account for 88% of the variance in LPFS scores. One factor reflects desirability of items (70%) and the other factor reflects scoring of the items (12%). I then show that the evaluative factor in the LPFS corelates highly, r = .9, with a similar evaluative factor in ratings of normal personality, when all items are scored in terms of desirability. Based on previous evidence from multi-method studies of normal personality, I interpret this factor as a response style that is unique to individual raters. Thus, most of the variance in LPFS scores reflects evaluative rating biases rather than levels of personality functioning. I also identified 10 items from the LPFS that are mostly free of actual personality variance, but correlate strongly with the evaluative factor. These items can be used as an independent measure of evaluative biases in self-ratings. The main conclusion of this article is that theories of personality disorders lack a clear concept and that self-report measures of personality disorders lack construct validity. Future research on personality disorders need to conduct more rigorous construct validation research with philosophically justifiable definitions of disorders and multi-method validation studies.

Introduction

A major problem in psychology is that it is too easy to make up concepts and theories about human behaviors that are based on overgeneralizations from single incidences or individuals to humans in general. A second problem is that pre-existing theories and beliefs often guide research and produce results that appear to confirm those pre-exist believes. A third problem is that psychology lacks a coherent set of rules to validate measures of psychological constructs (Markus & Borsboom, 2013). As a result, it is possible that large literatures are based on invalid measures (e.g., Schimmack, 2021). In this blog post, I will present evidence that an influential model of personality disorders is equally based on flawed measures.

What Are Personality Disorders?

The notion of personality disorders has a long history that predates modern conceptions of personality (Zacher, 2017). An outdated view, equated personality disorders with extreme – statistically abnormal – scores on measures of personality (Schneider, 1923). The problem with this definition of disorders is that abnormality can even be a sign of perfect functioning as in the performance of a Formula 1 race car or an Olympic athlete.

Personality disorders were formalized in the third Diagnostic and Statistical Manual of Mental Disorders, but the diagnosis of personality disorders remained controversial; at least, much more controversial than diagnosis of mental disorders with clear symptoms of dysfunction such as delusions and hallucinations. The current DSM-5 contains two competing models of personality disorders. Without a clear conception of personality disorders, the diagnosis of personality disorders remains controversial (Zacher, 2017).

A main obstacle in developing a scientific model of personality disorder is that historic models of personality disorders are difficult to reconcile with contemporary models of normal functioning personality that has emerged in the past decades. To achieve this goal, it may be necessary to start with a blank slate and rethink the concept of personality disorders.

Distinguishing Personality Disorders from (Normal) Personality

There is no generally accepted theory of personality. However, an influential model of personality assumes that individuals have different dispositions to respond to the same situation. These dispositions develop during childhood and adolescence in complex interactions between genes and environments that are poorly understood. By the beginning of early adulthood, these dispositions are fairly stable and change only relatively little throughout adulthood. While there are hundreds of dispositions that influence specific behaviors in specific situations, these dispositions are related to one or more of five broad personality dispositions that are called the Big Five. Neuroticism is a general dispositions to experience more negative feelings such as anxiety, anger, or sadness. Extraversion is a broad disposition to be more engaged that is reflected in sociability, assertiveness, and vigor. Openness is a general disposition to engage in mental activities. Agreeableness is a general disposition to care about others. Finally, conscientiousness is a general disposition to control impulses and persist in the pursuit of long-term goals. Variation along these personality traits is considered to be normal. Variation along these traits exists either because it has no major effect on life outcomes, the genetic effects are too complex to be subjected to selection, or because traits have different costs and benefits. This short description of normal personality is sufficient to discuss various models of personality disorders (Zachar & Krueger, 2013).

The vulnerabiltiy model of personality disorders can be illustrated with high neuroticism. High neuroticism is a predictor of lower well-being and a risk factor for the development of mood disorders. Even during times when individuals are not have clinical levels of anxiety or depression, they report elevated levels of negative moods. Thus, one could argue that high neuroticism is a personality disorder because it makes individuals vulnerable to suffer mental health problems. However, even in this example it is not clear whether neuroticism should be considered a risk factor for a disorder or a disorder itself. As many mood disorders are episodic, while neuroticism is stable, one could argue that neuroticism is a risk factor that only in combination with other factors (e.g., stress) triggers a disorder. The same is even more true for other personality traits. For example, low conscientiousness is one of several predictors of some criminal behaviors. This finding might be used to argue that low conscientiousness is a criterion to diagnose a personality disorder (e.g., psychopathy). However, it is also possible to think about low conscientiousness as a risk factor rather than a diagnostic feature of a personality disorder. In line with this argument, Zachner and Kruger (2013) suggest that “vulnerabilities are not disorders” (p. 1020). A simple analogy may suffice. White skin is a risk factor for skin cancer. This does not mean that White skin is a skin disease and it is possible to avoid the clinically relevant outcome of skin cancer by staying out of the sun, proper closing, or applying sun blockers. Even if we would recognize that personality can be a risk factor for various disorders, it would not justify the label of a personality disorder. The term implies that something about a person’s personality impedes their proper functioning. In contrast, the term risk factor merely implies that personality can contribute to the disfunction of something else.

The pathoplasticity model uses the term personality disorder for personality traits that influence the outcome of other psychiatric disorders. Zachar and Kruger (2013) suggest that people with a personality disorder develop mental health problems earlier in life or more often. This merely makes them risk factors, which were already discussed under the vulnerability model. More broadly personality traits may influence specific behaviors of patients suffering from mental health problems. For example, personality may influence whether depressed patients commit suicide or not. For example, men are more likely to commit suicide than women despite similar levels of depression. Understanding these personality effects is surely important for the treatment of patients, but it does not justify the label of personality disorders. In this example, the disorder is depression and treatment has to assess suicidality. The personality factors that influence suicidality are not part of the disorder.

The spectrum model views personality disorders as milder manifestations of more severe mental health problems that share a common cause. This model blurs the distinction between normal and disordered personality. At what level is anxiety still normal and at what level is it a mild manifestation of an anxiety disorder. A more reasonable distinction between normal and clinical anxiety is whether anxiety is rational (e.g., gun fire at a mall) or irrational (fear of being abducted by aliens). Models of normal personality traits are not able to capture these distinctions.

The decline-in-functioning model assumes that personality disorders are the result of traumatic brain injury, severe emotional trauma, or severe psychiatric disorder. As all behavior is regulated by the brain, brain damages can lead to dramatic changes in behavior. However, it seems odd to call these changes in behaviors a personality disorder. With regards to traumatic life events, it is not clear that they reliably produce major changes in personality. Avoidance after a traumatic injury is typically situation specific rather than a change in a broader general disposition. This model also ignores that the presence of a brain injury, other mental illnesses or drugs is used as an exclusion criterion to diagnose a personality disorder (Skodol et al., 2011).

The impairment-distress model more directly links personality to disorder or dysfunction. The basic assumption is that personality is associated with clinically significant impairment or distress. I think association is insufficient. For example, gender is corelated with neuroticism and the prevalence of anxiety disorders. It would be difficult to argue that this makes gender a personality disorder. To justify the notion of a personality disorder, personality needs to be a cause of distress and treatment of personality disorders should alleviate distress. Once more, high neuroticism might be the best candidate for a personality disorder. High neuroticism predicts higher levels of distress and treatment with anti-depressant medication or psychotherapy can lower neuroticism levels and distress levels. However, the impairment-distress model does not solve the problems of the vulnerability model. Is high neuroticism sufficient to be considered an impairment or is it merely a risk factor that can lead to impairment in combination with other factors?

This leaves the capacity-failure model as the most viable conceptualization of a personality disorder (Zachar, 2017). The capacity-failure model postulates that personality disorders represent dysfunctional deviations from the normal functions of personality. This model is a straightforward extension of conceptions of bodily functioning to personality. Organs and other body parts have clear functions and can be assessed in terms of their ability to carry out these functions (e.g., hearts pump blood). When organs are unable to perform these functions, patients are sick and suffer. Zachar (2017) points out a key problem of the extension of biological functions to personality. “The difficulty with all capacity failure models is that they rely on speculative inferences about normal, healthy functioning” (p. 1020). The reason is that personality refers to variation in systems and processes that serve a specific function. While the processes have a clear function, it is often less clear what function variation in these processes serves. Take anxiety as an example. Anxiety is a universal human emotion that evolved to alert people to potential danger. Humans without this mechanism might be considered to have a disorder. However, neuroticism reflects variation in the process that elicits anxiety. Some people are more sensitive and others are less sensitive to danger. To justify the notion of a personality disorder, it is not sufficient to specify the function of anxiety. It is also necessary to specify the function of variation in anxiety across individuals. This is a challenging task and current research on personality disorders has failed to specify personality functions to measure and diagnose personality disorders from a capacity-failure model.

To summarize, the reviewed conceptualizations of personality disorders provide insufficient justification for a distinction between normal personality and personality disorders. While some personality types may be associated with some negative outcomes, these correlations do not provide an empirical basis for a categorical distinction between personality and personality disorders. This leaves the capacity-failure model as the last option (Zachar, 2017). The capacity-failure model postulates that personality disorders represent dysfunctional deviations from the normal functions of personality. This model is a straightforward extension of conceptions of bodily functioning to personality. Organs and other body parts have clear functions and can be assessed in terms of their ability to carry out these functions (e.g., hearts pump blood). When organs are unable to perform these functions, patients are sick and suffer. Zachar (2017) points out a key problem of the extension of biological functions to personality. “The difficulty with all capacity failure models is that they rely on speculative inferences about normal, healthy functioning” (p. 1020). That is, while it is relatively easy to specify the function of body parts, it is difficult to specify the functions of personality traits. What is the function of extraversion or introversion? The key problem is that personality refers to variation in basic psychological processes. While we can specify the function of being selfish or altruistic, it is much harder to specify the function of having a disposition to be more selfish or more altruistic (agreeableness). However, without a clear function of these personality dispositions, it is impossible to define personality dysfunction. This is a challenging task and current research on personality disorders has failed to specify personality functions that could serve as a foundation for theories of personality disorders.

The Criterion-A Model of Personality Disoders

Given the lack of a theory of personality disorders, it is not surprising that personality disorder have conflicting views about the measurement of personality disorders (it is difficult to measure something, if you do not know what you are trying to measure). One group of researchers argues for a one-dimensional model of personality disorders that is called personality pathology severity (Morey, 2017; Morey et al., 2022). This model is based on the assumption that specific items or symptoms that are used to diagnose personality disorders are correlated and “show a substantial first or general factor” (p. 650). To measure this general dimension of personality disorder with self-ratings, Morey (2017) developed the Levels of Personality Functioning Scale–Self Report (LPFS–SR).

A major problem of this measure is the lack of a sound conceptual basis. That is, it is not clear what levels of personality functioning are. As noted before, it is not even clear what function individual personality traits have. It is much less clear what personality functioning is because personality is not a unidimensional trait. Take a car as an analogy. One could evaluate the functioning of a car and order cars in terms of their level of functioning. However, to do so, we would evaluate the functioning of all of the cars parts and the level of functioning would be a weighted sum of the checks for each individual part. The level of functioning does not exist independent of the functioning of the parts. For the diagnosis of cars it is entirely irrelevant whether functioning of one part is related to functioning of another part. A general factor of dysfunction might be present (newer cars are more likely to have functioning parts than older cars), but the general factor is not the construct of interest. The construct of dysfunction requires assessing the functioning of all parts that are essential for a car to carry out its function.

In short, the concept of levels of personality functioning is fundamentally flawed. Yet, validation studies claim that the levels of personality function scale is a valid measure of the severity of personality disorders (Hopwood et al., 2018). Unfortunately, validation research by authors who developed a test is often invalid because they only look for information that confirms their beliefs (Cronbach, 1989; Zimmermann, 2022). Ideally, validation research would be carried out by measurement experts who do not have a conflict of interest because they are not attached to a particular theory. In this spirit, I examined the construct validity of the level of psychological functioning scale, using Hopwood et al.‘s (2018) data (osf.io/v2s8u).

Structure of the LPFS-SR

Hopwood et al. (2018) did not conduct a factor analysis of the 80 LPFS-SR items. The omission of such a basic psychometric analysis is problematic even by the low standards of test validation in psychology (Markus & Borsboom, 2013). The reason might be that other researchers have already demonstrated that the assumed structure of the questionnaire does not fit the data (Sleep et al., 2020). Sleep et al. were also unable to find a model that fits the data. Thus, my analyses provide the first viable of the correlations among the LPFS-SR items. Viable, of course, does not mean perfect or true. However, the model provides important insights into the structure of the LPFS-SR and shows that many of the assumptions made by Morey (2017) are not supported by evidence.

I started with an exploratory factor analysis to examine the dimensionality of the LPFS-SR. Consistent with other analyses, I found that the LPFS-SR is multidimensional (Sleep et al., 2020). However, whereas Sleep et al. (2020) suggest that three or four factors might be sufficient, I found that even the Bayesian Information Criterion suggested 7 factors. Less parsimonious criteria suggested even more factors (Table 1).

I next examined whether the four-factor model corresponds to the theoretical assignment of items to the four scales. The criterion for model fit was that an item had the highest loading on the predicted factor and the factor loading was greater than .3. Using this criterion, only 33 of the 80 items had the expected factor loadings. Moreover, the correlations among the four factors were low. One factor had nearly zero correlations with the other three factors, r = .05 to .13. The correlations among the other three factors were moderate, r = .30 to .56, but do not support the notion of a strong general factor.

Exploratory factor analysis has serious limitations as a validation tool. For example, it is unable to model hierarchical structures, although Morey (2017) assumed a hierarchical structure with four primary and one higher-order factor. The most direct test of this model would require structural equation modeling (Confirmatory Factor Analysis). EFA also has problems separating content and method factors. As some of the items are reverse scored, it is most likely that acquiescence bias distorts the pattern of correlations. SEM can be used to specify an independent acquiescence factor to control for this bias (Anusic et al., 2009). Thus, I conducted more informative analysis with structural equation modeling (SEM) that are often called confirmatory factor analysis. However, the label confirmatory is misleading because it is seems to imply that SEM can only be used to confirm theoretical structures. However, the main advantage of SEM is that it is a highly flexible tool that can represent hierarchies, model method factors, and reveal residual correlations among items with similar content. This statistical tool can be used to explore data and to confirm models. A danger in exploratory use of CFA is overfitting. However, overfitting is mainly a problem for weak parameters that have little effect on the main conclusions. In my explorations, I set the minimum modification index to 20, which limits the type-I error probability to 1/129,128. Most parameters in the final model meet the 5-sigma criterion (z = 5, chi-square(1) = 25) that is used in particle physics to guard against type-I errors. Moreover, I posted all exploratory models (https://osf.io/uyrk7/) and I encourage others to improve on my model.

The final model (final.final.6) had acceptable fit according to the standard of .06 for the Root Mean Square Error of Approximation, RMSEA = .030. However, the Comparative Fit Index was below the criterion value of .95 that is often used to evaluate overall model fit, CFI = .922. Another way to evaluate the model is to compare it to the fit of the EFA models in Table 1. Accordingly, the model had better fit in a comparison of the Bayesian Information Criterion (179,033.304 vs. 181,643.255), Aikan’s Information Criterion (177,270,345 vs. 177,485.265), and RMSEA (.030 vs. 031), but not the CFI (.922 vs. 932). The difference between fit indices is explained by the trade-off between parsimony and precision. The CFA model is more parsimonious (2958 degrees of freedom) than the EFA model with 10-factors (2405 degrees of freedom). Using the remaining 554 degrees of freedom would produce even better fit, but at the risk of overfitting and none of the smaller MI suggested substantial changes to the model. The final model had 12 factors. that I will describe in order of their contribution to the variance in LPFS scale scores.

The most important factor is a general factor that showed notable positive loadings (> .3) for 64 of the 80 items (80%). This factor correlated r = .837 with the LPFS scale scores. Thus, 70% of the variance in scale scores reflects a single factor. This finding is consistent with the aim of the LPFS to measure predominantly a single construct of severity of personality functioning (y (Morey, 2017; Morey et al., 2022).). However, the presence of this factor does not automatically validate the measure because it is not clear whether this factor represents core personality functioning. An alternative interpretation of this factor assumes that it reflects a response style to agree more with desirable items that is known as socially desirable responding or halo bias (Anusic et al., 2009). I will examine this question later on when I relate LPFS factors to factors of normal personality.

The second factor reflects scoring of the items. All items were coded as directly coded (68) or reverse coded (12). For the sake of parsimony and identifiability, loadings on this factor were fixed to 1 or -1. Thus, all items loaded on this factor by definition. More important, this factor corelated r = .428 with LPFS scores. Thus, response sets explained another 18% of the variance in LPFS scores. Together, these two factors explained 70 + 18 = 82% of the total variance in LPFS scores.

The first content factor had 13 notable loadings (> .3). The highest loadings were for the items “Sometimes I am too harsh on myself” (.61), “The standards that I set for myself often seem to be too demanding, or not demanding enough” (.51)., and “I tend to feel either really good or really bad about myself.” (.483). This factor corelated only r = .154 with the LPFS scale scores. Thus, it adds at most 2% to the explained variance in LPFS scale scores. The contribution could be less because this factor is corelated with other content factors.

The second content factor had 8 notable loadings (> .3). The highest loadings were for the items “I have many satisfying relationships, both personally and on the job” (.487), “I work on my social relationships because they are important to me” (.445), and “Getting close to others just leaves me vulnerable and and isn’t worth the risk” (.440). This factor seems to capture investment in social relationships. The correlation of this factor with LPFS scores is r = .120 and the factor contributes at most 1.4% to the total variance of LPFS scores.

The third content factor had 6 notable loadings (> .3). The highest loadings were for the items “The key to a successful relationship is whether I get my needs met” (.490), “I’m only interested in relationships that can provide me with some comfort” (.476), “I can only get close to someone who can acknowledge and address my needs” (.416). This factor seems to reflect a focus on exchange versus communal relationships. It correlated r = .098 with LPFS scale scores and contributes less than 1% of the total variance in LPFS scores.

The 4th content factor had 7 notable loadings (> .3). The highest loadings were for the items “I have some difficulty setting goals” (.683), “I have difficulties setting and completing goals” (.639), and “I have trouble deciding between different goals” (.534). The item content suggests that this factor reflects problems with implementing goals. It correlates r = .070 with LPFS scores and explains less than 1% of the total variance in LPFS scores.

The 5th factor had only 3 notable loadings (> .3). The three items were “When others disapprove of me, it’s difficult to keep my emotions under control” (.572), “I have a strong need for others to approve of me” (..498), “In close relationships, it is as if I cannot live with the other person” (.334). This factor might be related to need for approval or anxious attachment. It correlates r = .057 with LPFS scores and explains less than 1% of the total variance in these scores.

The 6th factor had 4 notable loadings (> .3). The highest loadings were for the items “Feedback from others plays a big role in determining what is important to me” (.427), “My personal standards change quite a bit depending upon circumstances.” (.365), and “My motives are mainly imposed upon me, rather than being a personal choice.” (.322). This factor seems to capture a strong dependence on others. It correlates r = .050 with LPFS scores and contributes less than 1% of the total variance.

The 7th factor was a mini-factor with only three items and only one item had a loading greater than .3. The item was “My life is basically controlled by others.” The items of this factor all had secondary loadings on the previous factor, suggesting that it may be a method artifact and not a specific content factor. It correlated only r = .037 with LPFS scale scores and has a negligible contribution to the total variance in LPFS scores.

The 8th factor is also a mini-factor with only three items. Two items had notable loadings (> .3), namely “I can appreciate the viewpoint of other people even when I disagree with them” (.484) and “I can’t stand it when there are sharp differences of opinion” (. 379).

The 9th factor had 4 items with notable loadings (> .3), but two loadings were negative. The two items with positive loadings were “I don’t pay much attention to, or care very much about, the effect I have on other people” (.351) and “I don’t waste time thinking about my experiences, feelings, and actions” (.301). The two items with negative loadings were “My emotions rapidly shift around” (-.381) and “although I value close relationships, sometimes strong emotions get in the way” (-.319). This factor seems to capture emotionality. The correlation with LPFS scores is trivial, r = .008.

The 10th factor is also a mini-factor with only three items. Two items had notable loadings, namely “People think I am pretty good at reading the feelings and motives of others in
most situations” (-.567) and “I typically understand other peoples’ feelings better than they do (-.633). The content of these items suggests that the factor is related to emotional intelligence. Its correlation with LPFS scores is trivial, r = -.007.

In addition, there were 41 correlated residuals. Correlated residuals are essentially mini-factors with two items, but it is impossible to determine the loadings of items on these factors. Most of these correlated residuals were small (.1 to .2). Only two item pairs had correlated residuals greater than .3,, namely “I don’t have a clue about why other people do what they do” correlated with “I don’t understand what motivates other people at all” (.453) and “I can only get close to somebody who understands me very well” correlated with “I can only get close to someone who can acknowledge and address my needs” (..367). Whether these correlated residuals reflect important content that requires more items or whether they are merely method factors due to similar wording is an open question, but it does not affect the interpretation of the LPFS scores because these mini factors do not substantially contribute to the variance in LPFS scores.

The main finding is that the factor analysis of the LPFS items revealed 2 major factors and many minor factors. One of the major factors is a method factor that reflects scoring of the items. The other factor reflects a general disposition to score higher or lower on desirable attributes. This factor account for 70% of the total variance in LPFS scores. The important question is whether this factor reflects actual personality functioning – whatever this might be – or a response style to agree more strongly with desirable items and to disagree more with undesirable items.

Validation of the General Factor of the LPFS

A basic step in construct validation research is to demonstrate that correlations with other measures are consistent with theoretical expectations (Cronbach & Meehl, 1955; Markus & Borsboom, 2013; Schimmack, 2021). The focus is not only on positive correlations with related measures, but also the absence of correlations with measures that are not expected to be correlated. This is often called convergent and discriminant validity (Campbell & Fiske, 1959). Moreover, validity is a quantitative construct and the magnitude of correlations is also important. If the LPFS is a measure of core personality functioning it should corelate with life outcomes (convergent validity). This hypothesis could not be examined with these data because no life outcomes were measured. Anther prediction is that LPFS scores should not corelate with measures of response styles (discriminant validity). This hypothesis could be examined because the dataset contained a measure of the Big Five personality traits and it is possible to separate content and response styles in Big Five measures because multi-method studies show that the Big Five are largely independent (Anusic et al., 2009; Biesanz & West, 2004; Chang, Connelly, & Geeza, 2012; DeYoung, 2006). Additional evidence shows that the evaluative factor in personality ratings predicts self-ratings of well-being, but is a weak or no predictor of informant ratings of well-being (Kim, Schimmack, & Oishi, 2012; Schimmack & Kim, 2020). This is a problem for the interpretation of this factor as a measure of personality functioning because low functioning should produce distress that is notable to others. Thus, a high correlation between the evaluative factor in ratings of personality and personality disorder would suggest that the factor reflects a rating bias rather than personality functioning.

I first fitted a measurement model to the Big Five Inventory – 2 (Soto & John, 2017). In this case, it was possible to use a confirmatory approach because the structure of the BFI-2 is well-known. I modeled 15 primary factors with loadings on the Big Five factors as higher-order factors. In addition, the model included one factor for evaluative bias and one factor for acquiescence bias based on the scoring of items. This model had reasonable fit, but some problems were apparent. The conscientiousness facet “Responsibility” seemed to combine two separate facets that were represented by two items each. I also had problems with the first two items of the Agreeableness-facet Trust. Thus, these items were omitted from the model. These modifications are not substantial and do not undermine the interpretation of the factors in the model. The model also included several well-known secondary relationships. Namely, anxiety (N) and depression (N) had negative loadings on extraversion, respectfulness (A) had a negative loading on Extraversion, Assertiveness (E) had a negatively loading on Agreeableness, Compassion (A) had a positive loading on N, and Productiveness (C) had a positive loading on E. Finally, there were 5 pairs of correlated residuals due to similar item content. The fit of this final model (final.final.6.bfi) was acceptable, CFI = .906, RMSEA = .045.Only two primary loadings on the 15 facet factors were less than .4, but still greater than .3.

I then combined the two models without making any modifications to either model. The only additional parameters were used to relate the two models to each other. One parameter regressed the general factor of the LPFS model on the evaluative bias factor in the BFI model. Another one did the same for the two response style factors. Modification indices suggested several additional relationships that were added to the model. The fit of the final model (final.final.6) was acceptable, CFI = .875, RMSEA = .032. Difficulties with goal setting (LPFS content factor 4) was strongly negatively related to the productivity facet of conscientiousness, r = -.81, and slightly positively related to the compassion facet of agreeableness, r = .178. The Emotionality factor (LPFS content factor 9) was strongly correlated with Neuroticism, r = .776. The first content factor was also strongly correlated with the depression facet of neuroticism, r = .72, and moderately negatively correlated with agreeableness, r = -.264. The need for approval factor (content factor 5) was also strongly corelated with neuroticism, r = .608, and moderately negatively related to the assertiveness facet of agreeableness, r = -.249. Content factor 2 (“close relationships) was moderately negatively related to the trust facet of agreeableness, r = -.408, and weakly negatively related to the assertiveness facet of extraversion, r = -.117. A focus on exchange relationships (content factor 3) was moderately negatively correlated with agreeableness, r = -.379. Finally, content factor 10 had a moderate correlation with extraversion. In addition, 14 LPFS items had small to moderate loadings on some Big Five factors. Only three items had loadings greater than .3, namely “my emotions rapidly shift around” on Neuroticism, r = .404, “Sometimes I’m not very cooperative because other people don’t live up to my standards” on Agreeableness, and “It seems as if most other people have their life together more than I” on the depression facet of Neuroticism, r = .310.

These relationships imply that some of the variance in LPFS scores can be predicted from the BFI factors, but the effect sizes are small. Neuroticism correlates only r = .123 and explains only 1.5% of the variance in LPFS total scores. Correlations are also weak for Extraversion, r = -.104, Agreeableness, r = -.096, and Conscientiousness, r = -.045. Thus, if the LPFS is a measure of core personality functioning, we would have to assume that core personality functioning is largely independent of variation along the Big Five factors of normal personality.

In contrast to these weak relationships, the evaluative bias factor in self-ratings of normal personality is strongly correlated with the general factor of the LPFS scored in terms of higher desirability, r = .901. Given the strong contribution of the general factor to LPFS scores, it is not surprising that the evaluative factor of the Big Five explains a large amount of the variance in LPFS scores, r = .748. In this case, it is not clear whether the correlation coefficient should be squared because evaluative bias in BFI ratings is not a pure measure of evaluative bias. A model with more than two measures of evaluative bias would be needed to quantify how much a general – questionnaire independent – evaluative bias factor contributes to LPFS scores. Nevertheless, the present results confirm that the evaluative factor in ratings of normal personality is strongly related to the evaluative factor in ratings of personality disorders (McCabe, Oltmanns, & Widiger, 2022).

Making Lemonade: A New Evaluative Bias Measure

My analyses provide clear evidence that most of the variance in LPFS scores reflects a general evaluative factor that corelates strongly with an evaluative factor in ratings of normal personality. In addition, the analyses showed that only some items in the LPFS are substantially related to normal personality. This implies that many LPFS items measure desirability without measuring normal personality. This provides an opportunity to develop a measure of evaluative bias that is independent of normal personality. This measure can be used to control for evaluative bias in self-ratings. A new measure of evaluative bias would be highly welcome (to avoid the pun desirable) because existing social desirability scales lack validity, in part because they confound bias and actual personality content.

To minimize the influence of acquiescence bias, I tried to find an equal number of direct and reverse coded items. I selected items with high loadings on the evaluative factor and low loadings on the LPFS content factors or the Big Five factors. This produced a 10-item scale with 6 negative and 4 positive items.

Almost no close relationship turns out well in the end.
I can’t even imagine living a life that I would find satisfying.
I don’t have many positive interactions with other people.
I have little understanding of how I feel or what I do.
I tend to let others set my goals for me, rather than come up with them on my own.
I’m not sure exactly what standards I’ve set for myself.

I can appreciate the viewpoint of other people even when I disagree with them.
I work on my close relationships, because they are important to me.
I’m very aware of the impact I’m having on other people.
I’ve got goals that are reasonable given my abilities.

I added these 10 items to the Big Five model and specified a social desirability factor and an acquiescence factor. This model (final.final.6.bfi.sd) had acceptable fit, CFI = .892, RMSEA = .043. Three items had weak (< .3) loadings on one of the Big Five factors, indicating that the SD items were mostly independent of actual Big Five content. Thus, SD scores are practically independent of variance in normal personality as measured with the BFI-2. The correlation between the evaluative factor and the SD factor was r = .877 and the correlation with the SD scale as r = .79. This finding suggests that it is possible to capture a large portion of the evaluative variance in self-ratings of personality with the new 10-item social desirability scale. Future research with other measures of evaluative bias (cf. Anusic et al., 2009) and multi-method assessment of personality is needed before this measure can be used to control for socially desirable responding.

Discussion

Morey (2017) introduced the Levels of Personality Functioning Scale (LPFS) as a self-report measure of general personality pathology, core personality functioning, or the severity of personality dysfunction. Hopewood et al. (2018) conducted a validation study of the LPFS and concluded that their results support the validity of the LPFS. More recently, Morey et al. (2022) reiterate the claim that the LPFS has demonstrated strong validity. However, several commentaries pointed out problems with these claims (Sleep & Lynam, 2022). Sleep and Lynam (2022) suggested that the “LPFS may be assessing little more than general distress” (p. 326). They also suggested that overlap between LPFS content and normal personality content is a problem. As shown here as well, some LPFS items relate to neuroticism, conscientiousness, or agreeableness. However, it is not clear why this is a problem. It would be rather odd if core personality functioning were unrelated to normal personality. Moreover, the fact that some items are related to Big Five factors does not imply that the LPFS measures little more than normal personality. The present results show that LPFS scores are only weakly related to the Big Five factors. The real problem is that LPFS scores are much more strongly related to the evaluative factor in normal personality ratings than to measures of distress such as neuroticism or its depression facet.

A major shortcoming in the debate among clinical researchers interested in personality disorder is the omission of research on the measurement of normal personality. Progress in the measurement of normal personality was made in the early 2000s. when some articles combined multi-method measurement with latent variable modeling (Anusic et al., 2009; Biesanz & West, 2004; deYoung, 2006). These studies show that the general evaluative factor is unique to individual raters. Thus, it lacks convergent validity as a measure of a personality trait that is reflected in observable behaviors. The high correlation between this factor and the general factor in measures of personality disorders provides further evidence that the factor is a rater-specific bias rather than an disposition to display symptoms of sever personality disorders because dysfunction of personality is visible in social situations.

One limitation of the present study is that it used only self-report data. The interpretation of the general factor in self-ratings of normal personality is based on previous validation studies with multiple raters, but it would be preferable to conduct a multi-method study of the LPFS. The main prediction is that the general factor in the LPFS should show low convergent validity across raters. One study with self and informant ratings of personality disorders provided initial evidence for this hypothesis, but structural equation modeling would be needed to quantify the amount of convergent validity in evaluative variance across raters (Quilty, Cosentino, & Bagby, 2018).

In conclusion, while it is too early to dismiss the presence of a general factor of personality disorders, the present results raise serious concerns about the construct validity of the Level of Personality Functioning Scale. While LPFS scores reflect a general factor, it is not clear that this general factor corresponds to a general disposition of personality functioning. First, conceptual analysis questions the construct of personality functioning. Second, empirical analysis show that the general factor correlates highly with evaluative bias in personality ratings. As a result, researchers interested in personality disorders need to rethink the concept of personality disorders, use a multi-method approach to the measurement of personality disorders, and develop measurement models that separate substantive variance from response artifacts. They also need to work more closely with personality researches because a viable theory of personality disorders has to be grounded in a theory of normal personality functioning.

References

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Abstract (summary)

In a previous blog post (Schimmack, 2022), I estimated that affective balance (pleasure vs. pain) accounts for about 50% of the variance in subjective life-evaluations (life-satisfaction judgments). This suggests that respondents also use other information to evaluate their lives, but it is currently unclear what additional information respondents use to make life-satisfaction judgments. In this blog post, I analyzed data from Diener’s Second International Student Survey and found two additional predictors of life-satisfaction judgments, namely a general satisfaction factor (a disposition to report higher levels of satisfaction) and a weighted average of satisfaction with several life domains (financial satisfaction, relationship satisfaction, etc.). This key finding was robust across eight world regions. Another notable finding was that East Asians score much lower and Latin Americans score much higher on the general satisfaction factor than students from other world regions. Future research needs to uncover the causes of individual and cultural variation in general satisfaction.

Introduction

Philosophers have tried to define happiness for thousands of years (Sumner, 1996). These theories of the good life were objective theories that aimed to find universal criteria that make lives good. Despite some influential theories, this enterprise has failed to produce a consensual theory of the good life. One possible explanation for this disappointing outcome is that there is no universal and objective way to evaluate lives, especially in modern, pluralistic societies.

It may not be a coincidence that social scientists in the United States in the 1960s looked for alternative ways to study the good life. Rather than imposing a questionable objective definition of the good life on survey participants, they left it to their participants to define for themselves how their ideal life would look like. The first widely used subjective measure of well-being asked participants to rate their lives on a scale from 0 = worst possible life to 10 = best possible life. This measure is still used and is used in the Gallup World Poll to rank countries in terms of citizens’ average well-being.

Empirical research on subjective well-being might provide some useful information into philosophical attempts to define the good life (Kesebir & Diener, 2008). For example, hedonistic theories of well-being would predict that life-evaluations are largely determined by the amount of pleasure and pain that individuals experiences in their daily lives (Kahneman, 1999). In contrast, eudaimonic theories would receive some support from evidence that individuals’ subjective life-evaluations are based on doing good even if these good deeds do not increase pleasure. Of course, empirical data do not provide a simple answer to difficult and maybe unsolvable philosophical question, but it is equally implausible that a valid theory of well-being is unrelated to people’s evaluations of their lives (Sumner, 1996).

Although philosophers could benefit from empirical data and social scientists could benefit from the conceptual clarity of philosophy, attempts to relate the two are rare (Kesebir & Diener, 2008). This is not the place to examine the reasons for this lack of collaboration. Rather, I want to contribute to this important question by examining the predictors of life-satisfaction judgments. In a previous blog post, I reviewed 60-years of research to examine how much of the variance in subjective life-evaluations is explained by positive affect (PA) and negative affect (NA), the modern terms for the hedonic tone (good vs. bad) of everyday experiences (Schimmack, 2022). After taking measurement error into account, I found a correlation of r = .7 between affective balance (Positive Affect – Negative Affect) and subjective life-evaluations. By conventional standards in the social sciences, this is a strong correlation, suggesting that a good life is a happy life (Kesbir & Diener, 2003). However, a correlation of r = .7 implies that feelings explain only about half of the variance (we have to square .7 to get the amount of explained variance) in life-evaluations. This suggests that there is more to a good life than just feeling good. However, it is unclear what additional aspects of human lives contribute to subjective life-evaluations. To examine this question, I analyzed data from Diener’s Second International Student Survey (see, e.g., Kuppens, Realo, & Diener, 2008). Over 9,000 students from 48 different nations contributed to this study. Subjective life-evaluations were measured with Diener et al.’s (1985) Satisfaction with Life Scale. I only used the first three items because the last two items have lower validity, especially in cross-cultural comparisons (Oishi, 2006). Positive Affect was measured with two items (feeling happy, feeling cheerful). Negative Affect was measured with three items (angry, sad, and worried). The main additional predictors that might explain additional variance in life-satisfaction judgments were 18 questions about domain satisfaction. Domains ranged from satisfaction to self to satisfaction with textbooks. The main empirical question is whether domain satisfaction only predicts life-satisfaction because it increases affective balance. For example, good social relationships may increase PA and decrease NA. In this case, effects of social relationships on life-satisfaction would be explained by higher PA and lower NA, and satisfaction with social relationships would not make a unique prediction to life-satisfaction. However, satisfaction with grades might be different. Students might be satisfied with their lives if they get good grades , even if getting good grades does not increase PA or may even increase NA because studying and working hard is not always pleasurable.

The Structure of Domain Satisfaction

A common observation in studies of domain satisfaction is that satisfaction judgments in one domain tend to be positively correlated with satisfaction judgments in other domains. There are two explanations for this finding. One explanation is that personality factors influence satisfaction (Heller et al., 2004; Payne & Schimmack, 2021; Schneider & Schimmack, 2010). Individuals high in neuroticism or negative affectivity tend to be less satisfied with most life domains, especially those who are prone to depression (rather than anxiety). On the flip side, individuals who are prone to positive illusions tend to be more satisfied, presumably because they have overly positive perceptions of their lives (Schimmack & Kim, 2020). However, another factor that contributes to positive correlations among domain satisfaction ratings are response styles. Two individuals with the same level of satisfaction will use different numbers on the response scale. To separate personality effects and response styles is difficult and requires a measure of response styles or personality. This was not the case in this dataset. Thus, I was only able to identify a factor that reflects a general tendency to provide higher or lower satisfaction ratings without being able to identify the nature of this factor.

A simple way to identify a general satisfaction factor is to fit a bi-factor model to the data. I constrained the unstandardized loadings for all 18 domains to be equal. This model had good fit and only one modification index for financial satisfaction suggested a change to the model. Freeing this parameter showed a weaker loading for financial satisfaction. However, the general satisfaction factor was clearly identified. The remaining variances in the 18 domains still showed a complex pattern of correlations. The pattern of these correlations, however, is not particularly relevant for the present topic because the key question is how much of this remaining variance in domain satisfaction judgments contributes to subjective life-evaluations.

To examine this question, I used a formative measurement model. A formative measurement model is merely a weighted average of domains. The weights are empirically derived to maximize prediction of subjective life-evaluations. Thus, the 18 domain satisfaction judgments are used to create two predictors of subjective life-evaluations. One predictor is a general satisfaction factor that reflects a general tendency to report higher levels of satisfaction. The other predictor is the satisfaction in life domains after removing the influence of the general satisfaction factor.

Predicting Subjective Life-Evaluations

To examine whether the two domain satisfaction predictors add to the prediction of subjective life-evaluations, above and beyond PA and NA, I regressed LS on affective balance, general satisfaction, and domain satisfaction. I allowed for different coefficients across 7 world regions (Northern Europe/Anglo, Southern Europe, Eastern Europe, East Asia, South Asia, Latin America, & Africa). Table 1 shows the results.

The first finding is that all three predictors explain unique variance in subjective life-evaluations. This shows that the two domain satisfaction factors contribute to life-satisfaction judgments above and beyond affective balance. The second observation is that the general satisfaction factor is a stronger predictor than affective balance and the difference is significant in several regions (i.e., the 95% confidence intervals do not overlap, p < .01). Thus, it is important to study this powerful predictor of subjective life-evaluations in future research. Does it reveal personality effects or is it a mere response style? Finally, the weighted average of domain satisfaction is also a stronger predictor than affective balance except for Africa. This suggests that bottom-up effects of life domains contribute to life-evaluations. An important question for future research is to understand how life domains can be satisfying even if they do not produce high levels of pleasure or low levels of pain. Finally, there is considerable unexplained variance. Thus, future studies need to examine additional predictors of life-satisfaction judgments that produce this variation.

Table 2 shows the relationship of the general satisfaction factor with PA, NA, and affective balance. The key finding is that the general satisfaction factor was positively related to PA, negatively related to NA, and positively related to affective balance. This finding shows that the general satisfaction factor not only predicts unique variance in life-satisfaction judgments, but also predicts variance that is shared with affective balance. Thus, even well-being researchers who focus only on the shared variance between affective balance and life-satisfaction have to take the general satisfaction factor into account. The general satisfaction factor also contributes to the correlation between PA and NA. For example, for Anglo nations, the correlations of r = .50 with PA and r = -.55 imply a negative correlation of r = -.28 between PA and NA. An important question is how much of this relationship reflects real personality effects versus simple response styles.

Table 3 shows the results for the weighted average of domain satisfaction after removing the variance due to the general satisfaction factor. The pattern is similar, but the effect sizes are weaker, indicating that the general factor is more strongly related to affective balance than specific life domains.

In conclusion, domain satisfaction judgments can be divided into two components. One component represents a general disposition to provide higher satisfaction ratings. The other component represents satisfaction with specific life domains. Both components predict affective balance. In addition, both components predict subjective life-evaluations above and beyond affective balance. However, there remains substantial unexplained variance in life-satisfaction judgments that is unrelated to affective balance and satisfaction with life domains.

The contribution of Life Domains to the Weighted Average of Domain Satisfaction

Table 4 shows the domains that made a statistically significant contribution to the prediction of subjective life evaluations.

Strong effects (r > .3) are highlighted in green, whereas non-significant results are highlighted in red. The first observation is that subjective life-evaluations are influenced by many life domains with a small influence rather than a few life domains with a strong influence. This finding suggests that subjective life-evaluations do take a general picture rather than being influenced by a few, easily accessible life domains. The only exception was Africa where only two domains dominated the prediction of subjective life-evaluations. Whether this is a true cultural differences or a method problem remains to be examined in future research.

The second observation is that financial satisfaction and satisfaction with social relationships were the strongest and most consistent predictors of life-satisfaction judgments across world regions. These effects are consistent with evidence that changes in social relationships or income predict changes in life-satisfaction judgments (Diener, Lucas, & Scollon, 2006).

It is also important to remember that the difference between a statistically significant and a non-significant result is not itself statistically significant. Many of the confidence intervals are wide and overlap. Overall, the results suggest more similarity than differences across students from different world regions. Future research needs to examine whether some of the cultural differences are replicable. For example, academic abilities seem to be more important in both East and South Asia than in Latin America.

Regional Differences in Predictors of Subjective Well-Being

Table 5 shows the differences between world regions in the components that contribute to subjective life-evaluations. In this table values for global satisfaction are means, whereas the other values are intercepts that remove the influence of global satisfaction differences and domain specific differences for PA and NA and the influence of all predictors for life-satisfaction.

Red highlights show differences that imply lower well-being in comparison to the reference region Northern Europe/Anglo. The results are consistent with overall lower well-being in the other regions which is consistent with national representative surveys by Gallup.

Probably the most interesting finding is that East Asia has a very large negative difference for the global satisfaction factor. The complementary finding is Latin America’s high score on the general satisfaction factor. These finding are consistent with evidence that East Asia has lower well-being and Latin American nations have higher well-being than objective indicators of well-being like income predict. Thus, general satisfaction is likely to be a unique predictor of well-being above and beyond income and objective living conditions. The important question is whether this is merely a method artifact, as some have argued, or whether it is a real personality differences between cultures.

Summary

Social scientists started measuring subjective life-evaluations as well as positive and negative affective experiences in the 1960s. Sixty years of research have established that life-satisfaction judgments and the balance of PA and NA are strongly correlated in Western countries. The choice of affect items has a relatively small effect on the magnitude of the correlation. In contrast, systematic measurement error plays a stronger role. Systematic measurement error can inflate and attenuate true correlations. The existing results suggest that two sources of systematic measurement error have opposite effects. Evaluative bias inflates the observed correlation, but rater-specific measurement error attenuates the true correlation. The latter effect is stronger. As a result, multi-method studies produce stronger correlations. At present, I would interpret the data as evidence that the true correlation is around r =.7 +/- .2. (.5 to .9). This implies that affective balance explains about half of the variance in life-evaluations. Cross-cultural studies suggest that the true correlation might be lower in Asian cultures, but the difference is relatively small (.6 vs. .5, without controlling for systematic measurement error).

The finding that affective balance explains only some of the variance in life-satisfaction judgments raises an interesting new question that has not received much attention. What does lead to positive life-evaluations in addition to pleasure and pain? An exploration of this question requires the measurement of LS, PA and NA, and the specification of causal model with affective balance as a predictor of life-satisfaction. The few studies that have examined this question have found that domain satisfaction (Schimmack et al., 2002), intentional living (Busseri, 2015), and environmental mastery (Payne & Schimmack, 2021) are substantial unique predictors of subjective life-evaluations. These results are preliminary. Existing datasets and new studies can reveal additional predictors. Evidence of cultural variation in the importance of affective experiences needs to be replicated and additional moderators should be explored. Identifying a reliable set of predictors of life-satisfaction judgments can provide insights into individuals implicit definition of the good life. This information may be useful to evaluate objective theories of well-being and to evaluate the validity of life-satisfaction judgments as measures of subjective well-being. The present results are inconsistent with a view of humans as homo hedonimus, who only cares about affective experiences, but the results do suggest that pleasure and pain cannot be ignored in a theory of human well-being.

Literature Review

Positive Affect (PA) and Negative Affect (NA) are scientific constructs. People have expressed their feelings for thousands of years. Across many cultures, some emotion terms have similar meanings and are related to similar antecedents and consequences. However, I am not aware of any everyday expressions of feelings that use the terms Positive Affect or Negative Affect. Yet, the scientific concepts of PA and NA were created to make scientific claims about everyday experiences like happiness, sadness, fear, satisfaction, or frustration. The distinction between PA and NA implies that a major distinction between affects is that some affects are positive and others are negative. Yet, psychologists do not have a consensual definition of Positive Affect and Negative Affect.

While PA and NA were used occasionally in the scientific literature, the terms became popular after Bradburn developed the first measures of PA and NA and reported the results of empirical studies with Bradburn’s PA and NA scales . The first report did not even use the term affect and referred to the sales as measures of positive and negative feelings (Bradburn & Caplovitz, 1965). The terms positive affect and negative affect were introduced in the follow-up report (Bradburn, 1969).

To understand Bradburn’s concepts of PA and NA, it is useful to examine the social and historical context that led to the development of the first PA and NA scales. The scales were developed to “provide periodic inventories of the psychological well-being of the nations’ [USA] psychological well-being” (p. 1). However, the introduction also mentions the goal to “better understand the patterning of psychological adjustment” (p. 2) and “to determine the nature of mental health, as well as to determine the causes of mental illness” (p. 2). This sweeping agenda creates conceptual confusion because it is no longer clear how PA and NA are related to well-being and mental health. Although it is likely that PA and NA are related to some extent to well-being and mental health, it is unlikely that well-being or mental health can be defined in terms of PA and NA. Even if this were possible, it would only clarify the meaning of well-being and mental health, but not the meaning of PA and NA.

More helpful is Bradburn’s stated objected for developing his PA and NA scales. The goal was to “measure a wide range of pleasurable and unpleasurable experiences apt to be common in a heterogeneous population” (Bradburn & Caplovitz, 1965; p. 16). This statement of the objective makes it clear that Bradburn used the term positive affect to refer to pleasurable experiences and the term negative affect to refer to unpleasant experiences. Bradburn (1969) is even more explicit. His assumption for the validity of the self-report measure was that “people tend to code their experiences in terms of (among other things) their affective tone – positive, neutral, or negative. For our purposes, the particular content of the experience is not important. We are concerned with the pleasurable or unpleasurable character associated with the experience” (p. 54). Other passages also make it clear that Bradburn’s goal was to measure the hedonic tone of everyday experiences. In short, the distinction between PA and NA is based on the hedonic tone of the affective experiences. PA feels good and NA feels bad.

Bradburn’s (1969) final chapter provides the most important information about his sometimes implicit assumptions underlying his approach to the study of psychological well-being, mental health, or happiness. “We are implicitly stating our belief that the modern concept of mental health is really a concerns about the subjective sense of well-being, or what the Greeks called eudaimonia” (p. 225). It is also noteworthy that Bradburn did not reduce happiness to the balance of PA and NA. “By naming our forest “psychological well-being,” we have not meant to imply that concepts such as self-actualization, self-esteem, ego-strength, or autonomy, …., are irrelevant to our study… While we have said relatively little about these particular trees, we do not doubt that they are an integral and important part of the whole” (p. 224). Accordingly, Bradburn rejects the hedonistic idea that well-being can be reduced to the balance of pleasure and pain, but he assumed that PA and NA are important to the conception of a good life.

However, defining well-being in terms of PA, NA, and other good things in life is not a satisfactory definition of well-being. A complete theory of well-being would have to list the additional ingredients and justify their inclusion in a definition of well-being. Philosophers and some psychologists have tried to defend different conceptions of the good life (Sumner, 1996). The main limitation of these proposals is that it is difficult to defend one conception of the good life as superior to another. The key problem is that it is difficult to find a universal, objective criterion that can be used to evaluate individuals’ lives (Sumner, 1996).

One solution to this problem is to take a subjective perspective. Accordingly, individuals can chose their own ideals and evaluate their lives accordingly. In the 1960s, social scientists developed subjective measures of well-being. One of the first measures was Cantril’s ladder that asked respondents to place their actual lives on a ladder from 0 = worst possible life to 10 = best possible life. This measure does not impose any criteria on the life-evaluations. This measure continues to be used to this day. The measure is a subjective measure of well-being because respondents can use any information that they consider to be important to rate their lives. In theory, they could rely exclusively on the hedonic tone of their everyday experiences. In this case, we would expect a strong correlation between affective balance and life-evaluations. However, it is also possible that individuals follow other goals that do not aim to maximize pleasure and to minimize pain. In this case, the correlation between affective balance and life-evaluations would be attenuated. It is therefore interesting to examine empirically how much of the variance in life-evaluations or life-satisfaction judgments is explained by the hedonic tone of everyday experiences. Subsequently, I review the relevant studies that have examined this question over the past 50 years.

Bradburn (1969) simply states that “the difference between the numbers of positive and negative feelings is a good predictor of a person’s overall ratings of his own happiness” (p. 225), but he did not provide quantitative information about the amount of explained versus unexplained variance.

The next milestone in well-being research was Andrews and Whitey’s (1976) examination of the validity of well-being measures. They included Bradburn’s items, but modified the response format from a dichotomous yes/no format to a frequency format. They assumed that this might produce negative correlations between the PA and NA scales, but this expectation was not confirmed. More interesting is how much the balance of PA and NA correlated with subjective well-being ratings. The key finding was that affect balance scores correlated only r = .43 with a 7-point life-satisfaction rating, and r = .47 with a 7-point happiness scale, while the two global ratings correlated r = .63 with each other. Corrected for unreliability, this suggest that affective balance is strongly correlated with global life-evaluations, ((.43 + .47)/2)/sqrt(.63) = .57. Nevertheless, a substantial portion of the variance in global life-satisfaction judgments remains unexplained, 1-.57^2 = 68%. This finding undermines theories of well-being that define well-being exclusively in terms of the amount of PA and NA (Bentham, Kahneman, 1999). However, the evidence is by no means conclusive. Systematic measurement error in the PA and NA scales might severely attenuate the true influence of PA and NA on global life-evaluations, given the low convergent validity between self-ratings and informant ratings of affective experiences (Schneider & Schimmack, 2009).

Nearly a decade later, Diener (1984) published a highly influential review article on the field of subjective well-being research. In this article, he coined the term subjective well-being (SWB) for research on global life-satisfaction judgments and affective balance. SWB was defined as high life-satisfaction, high PA and low NA. Diener noted that the relationship among the three components of his SWB construct is an empirical question. He also pointed out that the relationship between PA and NA had received a lot of attention, whereas the relationship between affective balance and life-satisfaction “has not been as thoroughly researched” (p. 547). Surprisingly, this statement still rings true nearly 40 years later, despite a few attempts by Diener and his students, including myself, to study this relationship.

For the next twenty years, the relationship between PA and NA became the focus of attention and fueled a heated debate with proponents of independence (Watson, Clark, & Tellegen, 1988), bipolarity (Russell, 1980), and models of separate, yet negatively correlated dimensions (Diener, Smith, & Fujita, 1995). A general agreement is that time frame, response formats, and item selection influences the correlations among PA and NA measures (Watson, 1988). This raises a question about the validity of different PA and NA scales. If different scales produce different correlations between PA and NA, different scales may also produce different correlations between life-evaluations and affective balance. However, this question has not been systematically examined to this day.

To make matters worse, the debate about the structure of affect also led to confusion about the meaning of the terms PA and NA. Starting in the 1980s, Watson and colleagues started to use the terms as labels for the VARIMAX rotated first-two factors in exploratory factor analyses of correlations among affect ratings (Watson & Tellegen, 1985). They also used these labels for their Positive Affect and Negative Affect scales that were designed to measure these two factors (Watson, Clark, & Tellegen, 1988). They defined Positive Affect as a state of high energy, full concentration, and pleasurable engagement and Negative Affect as a state of subjective distress and unpleasurable engagement. An alternative model based on the unrotated factors, however, identifies a first factor that distinguishes affects based on their hedonic tone. Watson et al. (1988) refer to this factor as pleasantness-unpleasantness factor. Thus, PA is no longer equivalent with pleasant affect, and NA is no longer equivalent with unpleasant affect.

To avoid conceptual confusion, different labels have been proposed for measures that focus on hedonic tone and measures that focus on the PANAS dimensions. Some researchers have suggested to use pleasant affect and unpleasant affect for measures of hedonic tone. Others have proposed to label Watson and Tellegen factors Positive Activation and Negative Activation. In the broader context of research on well-being, PA and NA are often used in Bradburn’s tradition to refer to the hedonic tone of affective experiences, and I will follow in this tradition. I will refer to the PANAS scales as measures of Positive Activation and Negative Activation.

While it is self-evident that the PANAS scales are different from measures of hedonic tone, it is still possible that the difference between Positive Activation and Negative Activation is a good measure of affective balance. That is, individuals who often experience positive activation and rarely experience negative activation are in a pleasant affective state most of the time. In contrast, individuals who experience a lot of Negative Activation and rarely experience Positive Activation are expected to feel bad most of the time. Whether the PANAS scales are capable of measuring hedonic tone as well as other measures is an empirical question that has not been examined.

The next important article was published by Lucas, Diener, and Suh (1996). The authors aimed to examine the relationship between the cognitive component of SWB (i.e., life-satisfaction) and the affective component of SWB (i.e., PA and NA) using a multi-trait-multi-method approach (Campbell & Fiske, 1959). Study 1 used self-ratings and informant ratings of life-satisfaction on the Satisfaction with Life Scale and PANAS scores to examine this question. The key finding was that same-construct correlations were higher (i.e., LS r = .48, PA r = .43, NA r = .26) than different-construct correlations (i.e., LS-PA rs = .28, .31, LS-NA r = -.16, -.21, PA-NA r = -.02, -.14). This finding was interpreted as evidence that “life satisfaction is discriminable from positive and negative affect” (p. 616). The main problem with this conclusion is that the results do not directly examine the discriminant validity of life-satisfaction and affective balance. As affective balance is made up of two distinct components, PA and NA, it is self-evident that LS cannot be reduced to PA or NA alone. However, it is possible that life-satisfaction is strongly related to the balance of PA and NA. To examine this question it would have been necessary to compute an affective balance score or to use a latent variable model to regress life-satisfaction onto PA and NA. The latter approach can be applied to the published correlation matrix. I conducted a multiverse analysis with five different models that make different assumptions about the validity of self-ratings and informant ratings. The results were very similar and suggested that affective balance explains about half of the variance in life-satisfaction judgments, rs = .68 to .75. The higher amount of explained variance is partially explained by the lower validity of Bradburn’s scales (Watson, 1988) and partially due to the use of a multi-method approach as mono-method relationships were only r = .6, for self-ratings at Time 1, and r = .5, for self-ratings at time 2 (Lucas et al., 1996). In conclusion, Lucas et al.’s study provided evidence that life-satisfaction judgments are not redundant with affective balance when affective balance is measured with the PANAS scales. However, it is possible that other measures of PA and NA might be more valid and explain more variance in life-evaluations.

A couple of years later, Diener and colleagues presented the first article that focused on the influence of affective balance on life-satisfaction judgments (Suh, Diener, Oishi, & Triandis, 1998). The main focus of the article was cultural variation in the relationship between life-satisfaction and affective balance. Study 1 examined correlations in the World Value Survey that used Bradburn’s scales. Correlations with a single-item life-satisfaction judgment ranged from a maximum of r = .57 in West Germany to a minimum of r = .20 in Nigeria. The correlation for the US sample was r = .48, which closely replicates Andrews and Whitey’s results. Study 2 used the more reliable Satisfaction with Life Scale and hedonic items with an amount of time response format. This produced stronger correlations. The correlation for the US sample was r = .64. This is consistent with Lucas et al.’s (1996) mono-method results. This article suggested that affect contributes to subjective well-being, but does not determine it, and that culture moderates the use of affect in life-evaluations.

Diener and colleagues followed up on this finding, by suggesting that the influence of neuroticism and extraversion on subjective well-being is mediated by affective balance (Schimmack, Diener, & Oishi, 2002). The article also explored whether domain satisfaction might explain additional variance in life-satisfaction judgments. The key finding was that affective balance made a unique contribution to life-satisfaction judgments (b = .45), but two life-domains also made unique contributions (i.e., academic satisfaction, b = .27, romantic satisfaction, r = .23). Affective balance mediated the effects of extraversion and neuroticism. Schimmack et al. (2002) followed up on these findings by examining the mediating role of affective balance across cultures. They replicated Suh et al.’s (1998) finding that culture moderates the relationship between affective balance and life-satisfaction and found a strong relationship in the two Western cultures (US, German) in a structural equation model that controlled for random measurement error, r = .76. The stronger relationship might be due to the use of affect items that focus on hedonic tone.

The next big development in well-being research was the creation of Positive Psychology; the study of all things positive. Positive psychology promoted eudaimonic conceptions of well-being that are rooted in objective theories of well-being (Sumner, 1996). These theories clash with subjective theories of well-being that leave it to individuals to choose how they want to live their lives. An influential article by Keyes, Shmotkin, & Ryff (2002) pitted these two conceptions of well-being against each other, using the Midlife in the U.S. (MIDUS) sample (N = 3,032). The life-satisfaction item was Cantril’s ladder. The PA and NA items were ad-hoc items with an amount of time response format. This explains why the MIDUS PA and NA scales are strongly negatively correlated, r = -.62. PA and NA were also strongly correlated with LS, PA r = .52, NA r = -.46. The article did not examine the relationship between life-satisfaction and affective balance because the authors treated LS, PA, and NA as indicators of a latent variable. According to this model, neither life-satisfaction nor affective balance measure well-being. Instead, well-being is an unobserved construct that is reflected in the shared variance among LS, PA, and NA. Using the published correlations and assuming a reliability of .7 for the single-item life-satisfaction item (Busseri, 2015), I obtained a correlation of r = .66 between life-satisfaction and affective balance. This correlation is stronger than the correlation with the PANAS scales in Lucas et al.’s (1996) study, suggesting that hedonic PA and NA scales are more valid measures of hedonic tone of everyday experiences and produce correlations around r = .7 with life-satisfaction judgments in the United States.

In the 21st century, psychologists’ interest in the determinants of life-satisfaction judgments decreased for a number of reasons. Positive psychologists were more interested in exploring eudaimonic conceptions of well-being. They also treated life-satisfaction judgments as indicators of hedonic well-being and treated life-satisfaction judgments and affective measures as interchangeable indicators of hedonic well-being. Another blow to research on life-satisfaction was Kahneman’s suggestion that life-satisfaction judgments are unreliable and invalid (Kahneman, 1999; Schwarz & Strack, 1999) and his suggestion to focus on affective balance as the only criterion for well-being. Kahneman et al. (2006) reported that income predicted life-satisfaction judgments, but not measures of affective balance. However, this finding was not interpreted as a discovery that income influences well-being independently of affect, but rather as evidence that life-satisfaction judgments are invalid measures of well-being.

In contrast, sociologists continued to focus on subjective well-being and used life-satisfaction judgments as key indicators of well-being in important panel studies such as the General Social Survey, the German Socio-Economic Panel (SOEP), and the World Value Survey. Economists rediscovered happiness, but relied on life-satisfaction judgments to make policy recommendations (Diener, Lucas, Schimmack, & Helliwell, 2008). Although Gallup measures all three components of SWB, it relies exclusively on life-satisfaction judgments to rank nations in terms of happiness (World Happiness Reports, https://worldhappiness.report).

In 2008, I used data from a pilot study for the SOEP to replicate the finding that affective balance mediated the effects of extraversion and neuroticism (Schimmack, Schupp, & Wagner, 2008). The study also controlled for evaluative biases in self-ratings. In addition, unemployment and regional differences between former East and West Germany were unique predictors of life-satisfaction judgments. The unique effect of affective balance on life-satisfaction was r = .50. One reason for the weaker relationship is that the model controlled for shared method variance among life-satisfaction and affect ratings.

Kuppens, Realo, and Diener (2008) followed up on Suh et al.’s (1996) finding that culture moderates the relationship between affective balance and life-satisfaction. While they replicated that culture moderates the relationship, the use of a multi-level model with unstandardized scores made it difficult to assess the magnitude of these moderator effects. Furthermore, the authors examined moderation for the effects of PA and NA separately rather than evaluating cultural variation in the relationship between affective balance and life-satisfaction. Finally, the use of PA and NA scales makes it impossible to evaluate measurement equivalence across nations. Using the same data, I examined the relationship between affective balance and life-satisfaction using a multi-group structural equation model with a largely equivalent measurement model across 7 world regions (Northern Europe/Anglo, Southern Europe, Eastern Europe, East Asia, South Asia, Latin America, and Africa). I replicated that the correlation in Western countries is around r = .6 (Northern Europe/Anglo, r = .64, Southern Europe, r = .59). The weakest relationships were found in East Asia (r = .52) and South Asia (r = .51). While this difference was statistically significant, the effect size is rather small and suggests that affective balance contributes to life-satisfaction judgments in all cultures. A main limitation of this study is that it is unclear how much cultural differences in response styles contribute to the moderator effect. A comparison of the intercept of life-satisfaction (i.e., mean difference after controlling for mean differences in PA and NA) showed that all regions had lower life-satisfaction intercepts than the North-American/Anglo comparison group. This shows that factors unrelated to PA and NA (e.g., income, Kahneman et al., 2006) produce cultural variation in life-satisfaction judgments.

Zou, Schimmack, and Gere (2013) published a replication study of Lucas et al.’s sole multi-method study. The study was not a direct replication. Instead, it addressed several limitations in Lucas et al.’s study. Most importantly, it directly examined the relationship between life-satisfaction and affective balance. It also ensured that correlations are not attenuated by biases in life-satisfaction judgments by adding averaged domain satisfaction judgments as a predictor. The study also used hedonic indicators to measure PA and NA rather than assuming that the rotated Positive Activation and Negative Activation factors fully capture hedonic tone. Finally, the sample size was five times larger than in Lucas et al.’s study and included students and middle aged individuals (i.e., their parents). The results showed convergent and discriminant validity for life evaluations (global & averaged domain satisfaction), PA, and NA. Most important, the correlation between the life-evaluation factor and the affective balance factor was r = .90. While this correlation still leaves 20% unexplained variance in life-evaluations, it does suggest that the hedonic tone of life experiences strongly influences subjective life-evaluations. However, there are reasonable concerns that this correlation overestimates the importance of hedonic experiences. One problem is that judgments of hedonic tone over an extended period of time may be biased by life-evaluations. To address this concern it would be necessary to demonstrate that affect ratings are based on actual affective experiences rather than being inferred from life-evaluations.

Following a critical discussion of Diener’s SWB concept (Busseri & Sadava, 2011), Busseri tackled the issue empirically using the MIDUS data. To do so, Busseri (2015) examined how LS, PA, and NA are related to predictors of SWB. He explicitly examined which predictors may have a unique influence on life-satisfaction judgments above and beyond the influence of PA and NA. The main problem was that the chosen predictors had weak relationships with the well-being components. The main exception was the Intentional Living scale; that is, an average of ratings of how much effort respondents invest into work, finances, relationships, health, and life overall. This scale had a strong unique relationship with life-evaluations, b = .44, that was as strong as the unique effect of PA, b = .42, and stronger than the unique effect of NA, b = -.16. The study also replicated Kahneman et al.’s (2006) finding that income is a unique predictor of LS and unrelated to PA and NA, but even the effect of income is statistically small, b = .05. Using the published correlation matrix and correcting LS for unreliability, I found a correlation of r = .58 for LS and affective balance. The unique relationship after controlling for other predictors was r = .52, suggesting that most of the relationship between affective balance and life-satisfaction is direct and not spurious due to third variables that influence affective balance and life-satisfaction.

Payne and Schimmack (2022) followed up on Zou et al.’s (2013) study with a multiverse analysis. PA and NA were measured with different sets of items ranging from pure hedonic items (good, bad), happiness and sadness items, to models of PA and NA as higher order factors of several positive (joy, love, gratitude) and negative (anger, fear, sadness) affects (Diener et al., 1995). They also compared results for mono-method (only self-ratings) and multi-method (ratings by all three family members) measurement models. Finally, results were analyzed separately for students, mothers, and fathers as targets. They key finding was that item selection had a very small influence, whereas the comparison of mono-method and multi-method studies made a bigger difference. The mono-method results ranged from r = .64, 95%CI = .58 to .71 to r = .69, 95%CI = .63 to .75. The multi-method results ranged from r = .71, 95%CI = .62 to .81, to r = .86, 95%CI = .80 to .92. These estimates are somewhat lower than Zou et al.’s (2013) results and suggest that the true relationship is less than r = .9.

In Study 2, Payne and Schimmack (2022) conducted the first direct comparison of PANAS items with hedonic tone items using an online sample. They found that PANAS NA was virtually identical with other NA measures. This refutes the interpretation of PANAS NA as a measure of negative activation that is distinct from hedonic tone. However, PANAS PA was distinct from other PA measures and was a weaker predictor of life-evaluations. A latent variable model with the PANAS items produced a correlation of r = .78, 95%CI = .73 to .82. An alternative measure that focusses on hedonic tone, the Scale of Positive and Negative Experiences (SPANE, Diener & Bieswas-Diener, 2009) yielded a slightly stronger correlation, r = .83, 95% .79 to .86. In a combined model, the SPANE PA factor was a stronger predictor than the PANAS PA factor. Thus, PANAS scales are likely to underestimate the contribution of affect to life-evaluations, but the difference is small. The correlations might be stronger than in other studies due to the use of an online sample.

To summarize, correlations between affective balance and life-evaluations range from r = .5 to r = .9. Several methodological factors contribute to this variation, and studies that use more valid PA and NA scales and control for measurement error produce stronger correlations. In addition, culture can moderate this relationship but it is not clear whether culture influences response styles or actual differences in the contribution of affect to life-evaluations. A reasonable estimate of the true correlation is r = .7 (+/- .2), which suggests that about 50% of the variance in life-evaluations is accounted for by variation in the hedonic tone of everyday experiences. An important direction of future research is to identify the unique predictors of life-evaluations that explain the remaining variance in life-evaluations. Hopefully, it will not take another 60 years to get a better understanding of the determinants of individuals’ life-evaluations. A better understanding of life-satisfaction judgments is crucial for the construct validation of life-satisfaction judgments before they can be used to make claims about nations’ well-being and to make public policy recommendations.

For 30 years, I have been interested in cultural differences. I maintained a database of variables that vary across cultures, starting with Hofestede’s seminal rankings of 40 nations. Finding interesting variables was difficult and time consuming. The world has changed. Today it is easy to find interesting data on happiness, income, or type of government. Statistical software is also free (project R). This has changed the social sciences. Nowadays, the new problem is that data can be analyzed in many ways and that results can be inconclusive. As a result, social scientists can disagree even when the analyze the same data. Here I focus on predictors of national differences in happiness.

Happiness has been defined in many ways and any conclusion about national differences in happiness depends on the definition of happiness. The most widely used definition of happiness in the social sciences is subjective well-being. Accordingly, individuals define for themselves what they consider to be a good life and evaluate how close their actual lives are to their ideal lives. The advantage of this concept of well-being is that it does not impose values on the concept of happiness. Individuals in democratic countries could evaluate their lives based on different criteria than individuals in non-democratic countries. Thus, subjective well-being is not biased in favor of democracy, even though subjective conceptions of happiness emerged along with democracy in Western countries.

The most widely used measure of subjective well-being is Cantril’s ladder. Participants rate their lives on a scale from 0 = worst possible life to 10 = best possible life. This measure leaves it to participants to define what the worst or best possible life it. The best possible life in Denmark could be a very different life than the best possible life in Zimbabwe. Ratings on Cantril’s ladder are imperfect measures of subjective well-being and could distort comparisons of countries, but these ratings are currently used to compare the happiness of over 100 countries (WHR).

The Economist’s Intelligence Unit (EUI) has created ratings of countries’ forms of government that provides a measure of democracy (Democracy Index). Correlating the 2020 happiness means of countries with the democracy index produces a strong (linear) correlation of r = .68 (rank correlation r = .71).

This finding has been used to argue that democracies are better societies because they provide more happiness for their citizens (Williamson, 2022).

So the eastward expansion of democracy isn’t some US-led conspiracy to threaten Russia; it reflects the fact that, when given the choice, citizens tend to choose democracy and hope over autocracy and fear. They know instinctively that it brings a greater chance for happiness.

Although I am more than sympathetic to this argument, I am more doubtful that democracy alone is sufficient to produce more happiness. A strong correlation between democracy and happiness is insufficient to make this argument. It is well known that many predictors of nations’ happiness scores are strongly corelated with each other. One well known predictor is nations’ wealth or purchasing power. Money does buy essential goods. The best predictor of happiness is the median income per person that reflects the spending power of average citizens and is not distorted by international trade or rich elites.

While it is known that purchasing power is a predictor of well-being, it is often ignored how strong the relationship is. The linear correlation across nations is r = .79 (rank r = .82). It is often argued that the relationship between income is not linear and that money is more important in poorer countries. However, the correlation with log income is only slightly higher, r = .83.

This might suggest that purchasing power and democracy are both important for happiness. However, purchasing power and democracy are also strongly correlated, (linear r = .72, rank = .75). Multiple regression analysis can be used to see whether both variables independently contribute to the prediction of happiness.

Of course, dollars cannot be directly compared to ratings on a democracy index. To make the results comparable, I scored both variables from 0 for the lowest possible score to 1 for the highest possible score. For purchasing power, this variable ranged from Madagascar ($398) to Luxembourg ($26,321). For democracy, this variable ranged from Myanmar (1.02) to Norway (9.75).

The results show that purchasing power is a much stronger predictor of happiness than democracy.

The model predicts that a country with the lowest standing on purchasing power and democracy has a score of 3.63 on Cantril’s happiness measure. Increasing wealth to the maximum level without changing democracy would increase happiness to 3.63 + 3.13 = 6.76. In contrast, keeping purchasing power at the lowest level and increasing democracy to the highest level would increase happiness only to 3.63 + 0.48 = 4.11. One problem with statistical analyses across nations is that the sample size is limited by the number of nations. As a result, the positive relationship with democracy is not statistically significant and it is possible that the true effect is zero. In contrast, the effect of purchasing power is highly significant and it is unlikely (less than 5%) that the increase is less than 2.5 points.

Do these results imply that democracy is not very important for citizens’ happiness? Not necessarily. A regression analysis ignores the correlation between the predictor variables. It is possible that the correlation between purchasing power and democracy reflects at least in part a causal effect of democracy on wealth. For example, democratic governments may invest more in education and innovation and achieve higher economic growth. Democracies may also produce better working conditions and policies that benefit the working class rather than wealthy elites.

I will not repeat the mistake of many other social scientists to end with a strong conclusion that fits their world views based on weak and inconclusive data. The main aim of this blog post is to warn readers that social science is much more complicated than the natural sciences. Follow the science makes a lot of sense, when large clinical trials show strong effectiveness of drugs or vaccines. The social sciences can provide valuable information, but do not provide simple rules that can be followed to increase human well-being. This does not mean that social science is irrelevant. Ideally, social scientists would provide factual information and leave the interpretation to educated consumers.

In 1998, Anthony G. Greenwald and colleagues introduced the Implicit Association Test. Since then, Implicit Association Tests have been used in thousands of studies with millions of participants to study stereotypes and attitudes. The most prominent and controversial use of the race IAT that has been used to argue that many White Americans have more negative attitudes towards African Americans than they admit to others or even to themselves.

The popularity of IATs can be attributed to the use of IATs on the Project Implicit website that provides visitors of the website with the opportunity to take an IAT and to receive feedback about their performance. Over 1 million visitors have received feedback about their performance on the race IAT (Howell, Gaither, & Ratliff, 2015).

Providing participants with performance feedback can be valuable and educational. Coaches provide feedback to athletes so that they can improve their performance, and professors provide feedback about performance during midterms so that students can improve their performance on finals. However, the value of feedback depends on the accuracy of the feedback. As psychological researchers know, providing participants with false feedback is unethical and requires extensive debriefing to justify the use of false feedback in research. it is therefore crucial to examine the accuracy of performance feedback on the race IAT.

At face value, IAT feedback is objective and reflects participants’ responses to the stimuli that were presented during an IAT. However, this performance feedback should come with a warning that performance could vary across repeated administration of a test. For example, the retest reliability of performance on the race IAT has been estimated to be between r = .2 and r = .5. Even using a value of r = .5 implies that there is only a 75% probability that somebody with a score above average receives a score above average again on a second test (Rosenthal and Rubin, 1982).

However, the Project Implicit website gives the false impression that performance on IATs is rather consistent, while avoiding quantitative information about reliability.

Unreliability is not the only reason why performance feedback on the Project Implicit website could be misleading. Another problem is that visitors may be given the impression that performance on the race IAT reveals something about themselves that goes beyond performance on this specific task. One possible interpretation of race IAT scores is that they reveal implicit attitudes or evaluations of Black and White Americans. These implicit attitudes can be different from attitudes that individuals think they have that are called explicit attitudes. In fact, Greenwald et al. (1998) introduced IATs as a method that can detect implicit attitudes that can differ from explicit attitudes and this dual-attitude model has fueled interest in IATs.

The Project Implicit website does not provide a clear explanation of what Implicit association Tests test. Regarding the race IAT, visitors are told that it is not a measure of prejudice, but that it does measure their biases, even if these biases are not endorsed or contradict conscious beliefs.

However, other frequently asked question implies that IATs measure implicit stereotypes and attitudes. One question is how IATs measure implicit attitudes, implying that it can measure implicit attitudes (and that implicit attitudes exist).

Another one implies that performance on the race IAT reveals implicit attitudes that reflect cultural biases.

In short, while Project Implicit may not provide a clear explanation of what is being tested with an Implicit Association Test, it is strongly implied that test performance reveals something about participants’ racial biases that may contradict their self-perceptions.

An article by Howell, Gaither, and Ratliff (2015) makes this assumption explicit. This article examines how visitors of the Project Implicit website respond to performance feedback on the race IAT. The key claim of this article is that “people are generally defensive in response to feedback indicating that their implicit attitudes differ from their explicit attitudes” (p. 373). This statement rests on two assumptions. First, it makes the assumption of dual-attitude models that there are explicit and implicit attitudes, as suggested by Greenwald et al. (1998). Second, it implies that performance on a single race IAT provides highly valid information about implicit attitudes. These assumptions are necessary to place researchers in the position of an expert that know individuals’ implicit attitudes, just like a psychoanalyst is in a superior position to understand the true meaning of a dream. If test takers reject the truth, they are considered defensive because they are unwilling to accept the truth.

To measure defensiveness, Howell et al. (2015) used answers to three questions after visitors of the Project Implicit website received performance feedback on the race IAT, namely
(a) the IAT does not reflect anything about my thoughts or feelings unconscious or otherwise,
(b) whether I like my IAT score or not, it captures something important about me (reversed)
(c) the IAT reflects something about my automatic thoughts and feelings concerning this topic (reversed). Responses were made on a 1 = strongly disagree to 4 = strongly agree. On this scale, a score of 2.5 would imply neither agreement nor disagreement with the aforementioned statements.

There was hardly any difference in defensiveness scores between White (M = 2.31, SD = 0.68) Black (M = 2.38, SD = 0.74) or biracial (M = 2.33, SD = 0.73) participants. For White participants, a larger pro-White discrepancy was correlated with higher defensiveness scores, partial r = .16. The same result was found for Black participants, partial r = .13. A similar trend emerged for biracial participants. While these correlations are weak, they suggest that all three racial groups were less likely to believe in the accuracy of the feedback when the IAT scores showed a stronger pro-White bias than the self-ratings implied.

Howell et al. (2015) interpret these results as evidence of defensiveness. Accordingly, “White individuals want to avoid appearing racist (O’Brien et al., 2010) and Black individuals value pro-Black bias (Sniderman & Piazza, 2002)” (p. 378). However, this interpretation of the results rests on the assumption that the race IAT is an unbiased measure of racial attitudes. Howell et al. (2015) ignore a plausible alternative explanation of their results. The alternative explanation is that performance feedback on the race IAT is biased in favor of pro-White attitudes. One source of this bias could be the scoring of IATs which relies on the assumption that neutral attitudes correspond to a zero score. This assumption has been challenged in numerous articles (e.g., Blanton, Jaccard, Strauts, Mitchell, & Tetlock, 2015). It is also noteworthy that other implicit measures of racial attitudes show different results than the race IAT (Judd et al., 1995; Schimmack & Howard, 2021). Another problem is that there is little empirical support for dual-attitude models (Schimmack, 2021). Thus, it is impossible for IAT scores to provide truthful information that is discrepant from individuals’ self-knowledge (Schimmack, 2021).

Of course, people are defensive when they are confronted with unpleasant information and inconvenient truths. A prime example of defensiveness is the response of the researchers behind Project Implicit to valid scientific criticism of their interpretation of IAT scores.

Despite several inquires about questionable or even misleading statements on the frequently asked question page, Project Implicit visitors are not informed that the wider scientific community has challenged the interpretation of performance feedback on the race IAT as valid information about individuals implicit attitudes. The simple fact that a single IAT score provides insufficient information to make valid claims about an individuals’ attitudes or behavioral tendencies is missing. Visitors should be informed that the most plausible and benign reason for a discrepancy between their test scores and their beliefs is that test scores could be biased. However, Project Implicit is unlikely to provide visitors with this information because the website is used for research purposes and willingness to participate in research might decrease when participants are told the truth about the mediocre validity of IATs.

Proponents of IATs often argue that taking an IAT can be educational. However, Howell et al. (2015) point out that even this alleged benefit is elusive because individuals are more likely to believe themselves than the race IAT feedback. Thus, rejection of IAT feedback, whether it is based on defensiveness or valid concerns about the validity of the test results, might undermine educational programs that aim to reduce actual racial biases. It is therefore problematic to use the race IAT in education and intervention programs.

Since 2011, it is an open secret that many published results in psychology journals do not replicate. The replicability of published results is particularly low in social psychology (Open Science Collaboration, 2015).

A key reason for low replicability is that researchers are rewarded for publishing as many articles as possible without concerns about the replicability of the published findings. This incentive structure is maintained by journal editors, review panels of granting agencies, and hiring and promotion committees at universities.

To change the incentive structure, I developed the Replicability Index, a blog that critically examined the replicability, credibility, and integrity of psychological science. In 2016, I created the first replicability rankings of psychology departments (Schimmack, 2016). Based on scientific criticisms of these methods, I have improved the selection process of articles to be used in departmental reviews.

1. I am using Web of Science to obtain lists of published articles from individual authors (Schimmack, 2022). This method minimizes the chance that articles that do not belong to an author are included in a replicability analysis. It also allows me to classify researchers into areas based on the frequency of publications in specialized journals. Currently, I cannot evaluate neuroscience research. So, the rankings are limited to cognitive, social, developmental, clinical, and applied psychologists.

2. I am using department’s websites to identify researchers that belong to the psychology department. This eliminates articles that are from other departments.

3. I am only using tenured, active professors. This eliminates emeritus professors from the evaluation of departments. I am not including assistant professors because the published results might negatively impact their chances to get tenure. Another reason is that they often do not have enough publications at their current university to produce meaningful results.

Like all empirical research, the present results rely on a number of assumptions and have some limitations. The main limitations are that
(a) only results that were found in an automatic search are included
(b) only results published in 120 journals are included (see list of journals)
(c) published significant results (p < .05) may not be a representative sample of all significant results
(d) point estimates are imprecise and can vary based on sampling error alone.

These limitations do not invalidate the results. Large difference in replicability estimates are likely to predict real differences in success rates of actual replication studies (Schimmack, 2022).

University of Amsterdam

The University of Amsterdam is the highest ranked European psychology department (QS Rankings). I used the department website to find core members of the psychology department. I found 48 senior faculty members. Not all researchers conduct quantitative research and report test statistics in their result sections. Therefore, the analysis is limited to 25 faculty members that had at least 100 test statistics.

A search of the database retrieved 13,529 test statistics. This is the highest number of statistical tests for all departments examined so far (Department Rankings). This partially explains the high ranking of the University of Amsterdam in rankings of prestige.

Figure 1 shows the z-curve plot for these results. I use the Figure to explain how a z-curve analysis provides information about replicability and other useful meta-statistics.

1. All test-statistics are converted into absolute z-scores as a common metric of the strength of evidence (effect size over sampling error) against the null-hypothesis (typically H0 = no effect). A z-curve plot is a histogram of absolute z-scores in the range from 0 to 6. The 2,034 z-scores greater than 6 are not shown because z-scores of this magnitude are extremely unlikely to occur when the null-hypothesis is true (particle physics uses z > 5 for significance). Although they are not shown, they are included in the computation of the meta-statistics.

2. Visual inspection of the histogram shows a drop in frequencies at z = 1.96 (solid red line) that corresponds to the standard criterion for statistical significance, p = .05 (two-tailed). This shows that published results are selected for significance. The dashed red line shows significance for p < .10, which is often used for marginal significance. Thus, there are more results that are presented as significant than the .05 criterion suggests.

3. To quantify the amount of selection bias, z-curve fits a statistical model to the distribution of statistically significant results (z > 1.96). The grey curve shows the predicted values for the observed significant results and the unobserved non-significant results. The statistically significant results (including z > 6) make up 35% of the total area under the grey curve. This is called the expected discovery rate because the results provide an estimate of the percentage of significant results that researchers actually obtain in their statistical analyses. In comparison, the percentage of significant results (including z > 6) includes 70% of the published results. This percentage is called the observed discovery rate, which is the rate of significant results in published journal articles. The difference between a 70% ODR and a 35% EDR provides an estimate of the extent of selection for significance. The difference of ~35 percentage points is large in absolute terns, but relatively small in comparison to other psychology departments. The upper level of the 95% confidence interval for the EDR is 46%. Thus, the discrepancy is not just random. To put this result in context, it is possible to compare it to the average for 120 psychology journals in 2010 (Schimmack, 2022). The ODR (70% vs. 72%) is similar, but the EDR is higher (35% vs. 28%), suggesting less severe selection for significance by faculty members at the University of Amsterdam that are included in this analysis.

4. The z-curve model also estimates the average power of the subset of studies with significant results (p < .05, two-tailed). This estimate is called the expected replication rate (ERR) because it predicts the percentage of significant results that are expected if the same analyses were repeated in exact replication studies with the same sample sizes. The ERR of 66% suggests a fairly high replication rate. The problem is that actual replication rates are lower than the ERR predictions (about 40% Open Science Collaboration, 2015). The main reason is that it is impossible to conduct exact replication studies and that selection for significance will lead to a regression to the mean when replication studies are not exact. Thus, the ERR represents the best case scenario that is unrealistic. In contrast, the EDR represents the worst case scenario in which selection for significance does not select more powerful studies and the success rate of replication studies is not different from the success rate of original studies. The EDR of 35% is below the actual replication success rate of 40%. To predict the success rate of actual replication studies, I am using the average of the EDR and ERR, which is called the actual replication prediction (ARP). For the University of Amsterdam, the ARP is (70 +35)/2 = 53%. This is somewhat higher than the currently best estimate of the success rate for actual replication studies based on the Open Science Collaboration project (~40%). Thus, research from the University of Amsterdam is expected to replicate at a higher rate than the replication rate for psychology in general.

5. The EDR can be used to estimate the risk that published results are false positives (i.e., a statistically significant result when H0 is true), using Soric’s (1989) formula for the maximum false discovery rate. An EDR of 35% implies that no more than 10% of the significant results are false positives, but the lower limit of the 95%CI of the EDR, 23%, allows for 18% false positive results. One solution to this problem is to lower the conventional criterion for statistical significance (Benjamin et al., 2017). Figure 2 shows that alpha = .005 reduces the point estimate of the FDR to 2% with an upper limit of the 95% confidence interval of 4%. Thus, without any further information readers could use this criterion to interpret results published in articles by psychology researchers at Western University.

Some researchers have changed research practices in response to the replication crisis. It is therefore interesting to examine whether replicability of newer research has improved. It is particularly interesting to examine changes at the University of Amsterdam because Erik-Jan Wagenmakers, a faculty member in the Methodology department, is a prominent advocate of methodological reforms. To examine this question, I performed a z-curve analysis for articles published in the past five year (2016-2021).

The results are disappointing. There is no evidence that research practices have changed in response to concerns about replication failures. The EDR estimate dropped from 35% to 25%, although this is not a statistically significant change. The ERR also decreased slightly from 72% to 69%. Therefore, the predicted success rate for actual replication studies decreased from 51% to 47%. This means that the University of Amsterdam decreased in rankings that focus on the past five years because some other departments have improved.

The replication crisis has been most severe in social psychology (Open Science Collaboration, 2015) and was in part triggered by concerns about social psychological research in the Netherlands. I therefore also conducted a z-curve analysis for the 10 faculty members in social psychology. The EDR is lower (24% vs. 35%) than for the whole department, which also implies a lower actual replication rate and a higher false positive risk.

There is variability across individual researchers, although confidence intervals are often wide due to the smaller number of test statistics. The table below shows the meta-statistics of all faculty members that provided results for the departmental z-curve. You can see the z-curve for individual faculty member by clicking on their name.

Rank	Name	ARP	EDR	ERR	FDR
1	Jaap M. J. Murre	77	81	74	2
2	Hilde M. Geurts	73	76	69	2
3	Timo Stein	73	76	70	2
4	Hilde M. Huizenga	68	75	61	3
5	Maurits W. van der Molen	65	72	57	4
6	Astrid C. Homan	62	69	55	4
7	Wouter van den Bos	60	74	47	6
8	Frenk van Harreveld	54	64	44	7
9	Gerben A. van Kleef	53	70	37	9
10	K. Richard Ridderinkhof	53	69	36	9
11	Bruno Verschuere	52	72	32	11
12	Maartje E. J. Raijmakers	51	74	28	13
13	Merel Kindt	48	62	35	10
14	Mark Rotteveel	47	59	34	10
15	Sanne de Wit	47	74	20	22
16	Susan M. Bogels	44	63	26	15
17	Matthijs Baas	44	62	25	16
18	Arnoud R. Arntz	43	68	17	26
19	Filip van Opstal	43	65	20	20
20	Suzanne Oosterwijk	42	56	29	13
21	Edwin A. J. van Hooft	40	65	15	30
22	E. J. B. Doosje	38	61	15	31
23	Nils B. Jostmann	37	48	26	15
24	Barbara Nevicka	37	59	14	33
25	Reinout W. Wiers	36	47	25	15

Since 2011, it is an open secret that many published results in psychology journals do not replicate. The replicability of published results is particularly low in social psychology (Open Science Collaboration, 2015).

A key reason for low replicability is that researchers are rewarded for publishing as many articles as possible without concerns about the replicability of the published findings. This incentive structure is maintained by journal editors, review panels of granting agencies, and hiring and promotion committees at universities.

To change the incentive structure, I developed the Replicability Index, a blog that critically examined the replicability, credibility, and integrity of psychological science. In 2016, I created the first replicability rankings of psychology departments (Schimmack, 2016). Based on scientific criticisms of these methods, I have improved the selection process of articles to be used in departmental reviews.

1. I am using Web of Science to obtain lists of published articles from individual authors (Schimmack, 2022). This method minimizes the chance that articles that do not belong to an author are included in a replicability analysis. It also allows me to classify researchers into areas based on the frequency of publications in specialized journals. Currently, I cannot evaluate neuroscience research. So, the rankings are limited to cognitive, social, developmental, clinical, and applied psychologists.

2. I am using department’s websites to identify researchers that belong to the psychology department. This eliminates articles that are from other departments.

3. I am only using tenured, active professors. This eliminates emeritus professors from the evaluation of departments. I am not including assistant professors because the published results might negatively impact their chances to get tenure. Another reason is that they often do not have enough publications at their current university to produce meaningful results.

Like all empirical research, the present results rely on a number of assumptions and have some limitations. The main limitations are that
(a) only results that were found in an automatic search are included
(b) only results published in 120 journals are included (see list of journals)
(c) published significant results (p < .05) may not be a representative sample of all significant results
(d) point estimates are imprecise and can vary based on sampling error alone.

These limitations do not invalidate the results. Large difference in replicability estimates are likely to predict real differences in success rates of actual replication studies (Schimmack, 2022).

Western University

I used the department website to find core members of the psychology department. I found 35 faculty members at the associate (9) or full professor (26) level. Not all researchers conduct quantitative research and report test statistics in their result sections. Therefore, the analysis is limited to 14 faculty members that had at least 100 test statistics.

Figure 1 shows the z-curve for all 6,080 tests statistics. I use the Figure to explain how a z-curve analysis provides information about replicability and other useful meta-statistics.

1. All test-statistics are converted into absolute z-scores as a common metric of the strength of evidence (effect size over sampling error) against the null-hypothesis (typically H0 = no effect). A z-curve plot is a histogram of absolute z-scores in the range from 0 to 6. The 865 z-scores greater than 6 are not shown because z-scores of this magnitude are extremely unlikely to occur when the null-hypothesis is true (particle physics uses z > 5 for significance). Although they are not shown, they are included in the computation of the meta-statistics.

2. Visual inspection of the histogram shows a drop in frequencies at z = 1.96 (solid red line) that corresponds to the standard criterion for statistical significance, p = .05 (two-tailed). This shows that published results are selected for significance. The dashed red line shows significance for p < .10, which is often used for marginal significance. Thus, there are more results that are presented as significant than the .05 criterion suggests.

3. To quantify the amount of selection bias, z-curve fits a statistical model to the distribution of statistically significant results (z > 1.96). The grey curve shows the predicted values for the observed significant results and the unobserved non-significant results. The statistically significant results (including z > 6) make up 38% of the total area under the grey curve. This is called the expected discovery rate because the results provide an estimate of the percentage of significant results that researchers actually obtain in their statistical analyses. In comparison, the percentage of significant results (including z > 6) includes 70% of the published results. This percentage is called the observed discovery rate, which is the rate of significant results in published journal articles. The difference between a 70% ODR and a 38% EDR provides an estimate of the extent of selection for significance. The difference of ~30 percentage points is large in absolute terns, but relatively small in comparison to other psychology departments. The upper level of the 95% confidence interval for the EDR is 56%. Thus, the discrepancy is not just random. To put this result in context, it is possible to compare it to the average for 120 psychology journals in 2010 (Schimmack, 2022). The ODR (70% vs. 72%) is similar, but the EDR is higher (38% vs. 28%), suggesting less severe selection for significance for research published by faculty members at Western University included in this analysis.

4. The z-curve model also estimates the average power of the subset of studies with significant results (p < .05, two-tailed). This estimate is called the expected replication rate (ERR) because it predicts the percentage of significant results that are expected if the same analyses were repeated in exact replication studies with the same sample sizes. The ERR of 70% suggests a fairly high replication rate. The problem is that actual replication rates are lower than the ERR predictions (about 40% Open Science Collaboration, 2015). The main reason is that it is impossible to conduct exact replication studies and that selection for significance will lead to a regression to the mean when replication studies are not exact. Thus, the ERR represents the best case scenario that is unrealistic. In contrast, the EDR represents the worst case scenario in which selection for significance does not select more powerful studies and the success rate of replication studies is not different from the success rate of original studies. The EDR of 38% is closer to the actual replication success rate of 40%. To predict the success rate of actual replication studies, I am using the average of the EDR and ERR, which is called the actual replication prediction (ARP). For Western University, the ARP is (70 +38)/2 = 54%. This is close to the currently best estimate of the success rate for actual replication studies based on the Open Science Collaboration project (~40%). Thus, research from Western University is expected to replicate at the average rate of actual replication studies.

5. The EDR can be used to estimate the risk that published results are false positives (i.e., a statistically significant result when H0 is true), using Soric’s (1989) formula for the maximum false discovery rate. An EDR of 38% implies that no more than 9% of the significant results are false positives, but the lower limit of the 95%CI of the EDR, 23%, allows for 18% false positive results. One solution to this problem is to lower the conventional criterion for statistical significance (Benjamin et al., 2017). Figure 2 shows that alpha = .005 reduces the point estimate of the FDR to 1% with an upper limit of the 95% confidence interval of 3%. Thus, without any further information readers could use this criterion to interpret results published in articles by psychology researchers at Western University.

Some researchers have changed research practices in response to the replication crisis. It is therefore interesting to examine whether replicability of newer research has improved. To examine this question, I performed a z-curve analysis for articles published in the past five year (2016-2021).

The results are amazing. The EDR increased to 70% with a relatively tight confidence interval ranging from 61% to 78%. The confidence interval does not overlap with the confidence interval for all-time z-scores. This makes Western only the second department that shows a statistically significant improvement in response to the replication crisis. Moreover, The ARP of 74% is the highest and much higher than some other departments.

There is variability across individual researchers, although confidence intervals are often wide due to the smaller number of test statistics. The table below shows the meta-statistics of all faculty members that provided results for the departmental z-curve. You can see the z-curve for individual faculty member by clicking on their name.

Rank	Name	ARP	EDR	ERR	FDR
1	Rachel M. Calogero	80	88	71	2
2	Melvyn A. Goodale	74	78	70	2
3	Daniel Ansari	67	77	58	4
4	John Paul Minda	64	75	54	5
5	Stefan Kohler	63	66	60	3
6	Ryan A. Stevenson	57	65	50	5
7	Debra J. Jared	54	76	33	11
8	Erin A. Heerey	52	64	41	8
9	Stephen J. Lupker	51	69	33	11
10	Ken McRae	51	69	32	11
11	Ingrid S. Johnsrude	49	75	22	18
12	Lorne Campbell	45	62	29	13
13	Marc F. Joanisse	45	67	24	17
14	Victoria M. Esses	39	52	26	15

Since 2011, it is an open secret that many published results in psychology journals do not replicate. The replicability of published results is particularly low in social psychology (Open Science Collaboration, 2015).

A key reason for low replicability is that researchers are rewarded for publishing as many articles as possible without concerns about the replicability of the published findings. This incentive structure is maintained by journal editors, review panels of granting agencies, and hiring and promotion committees at universities.

To change the incentive structure, I developed the Replicability Index, a blog that critically examined the replicability, credibility, and integrity of psychological science. In 2016, I created the first replicability rankings of psychology departments (Schimmack, 2016). Based on scientific criticisms of these methods, I have improved the selection process of articles to be used in departmental reviews.

1. I am using Web of Science to obtain lists of published articles from individual authors (Schimmack, 2022). This method minimizes the chance that articles that do not belong to an author are included in a replicability analysis. It also allows me to classify researchers into areas based on the frequency of publications in specialized journals. Currently, I cannot evaluate neuroscience research. So, the rankings are limited to cognitive, social, developmental, clinical, and applied psychologists.

2. I am using department’s websites to identify researchers that belong to the psychology department. This eliminates articles that are from other departments.

3. I am only using tenured, active professors. This eliminates emeritus professors from the evaluation of departments. I am not including assistant professors because the published results might negatively impact their chances to get tenure. Another reason is that they often do not have enough publications at their current university to produce meaningful results.

Like all empirical research, the present results rely on a number of assumptions and have some limitations. The main limitations are that
(a) only results that were found in an automatic search are included
(b) only results published in 120 journals are included (see list of journals)
(c) published significant results (p < .05) may not be a representative sample of all significant results
(d) point estimates are imprecise and can vary based on sampling error alone.

These limitations do not invalidate the results. Large difference in replicability estimates are likely to predict real differences in success rates of actual replication studies (Schimmack, 2022).

McGill University

I used the department website to find core members of the psychology department. I found (only) 20 faculty members at the associate (5) or full professor (15) level. The reason is that McGill is going through a phase of renewal and currently has a large number of assistant professors before tenure that are not included in these analyses (14). It will be interesting to see the replicability of research at McGill in five years when these assistant professors are promoted to the rank of associate professor.

Not all researchers conduct quantitative research and report test statistics in their result sections. Therefore, the analysis is limited to 10 faculty members that had at least 100 significant test statistics. Thus, the results are by no means representative of the whole department with 34 faculty members, but I had to follow the same criteria that I used for other departments.

Figure 1 shows the z-curve for all 3,000 tests statistics. This is a relatively small number of z-scores. Larger departments and departments with more prolific researchers can have over 10,000 test statistics. I use the Figure to explain how a z-curve analysis provides information about replicability and other useful meta-statistics.

1. All test-statistics are converted into absolute z-scores as a common metric of the strength of evidence (effect size over sampling error) against the null-hypothesis (typically H0 = no effect). A z-curve plot is a histogram of absolute z-scores in the range from 0 to 6. The 412 z-scores greater than 6 are not shown because z-scores of this magnitude are extremely unlikely to occur when the null-hypothesis is true (particle physics uses z > 5 for significance). Although they are not shown, they are included in the computation of the meta-statistics.

2. Visual inspection of the histogram shows a steep drop in frequencies at z = 1.96 (solid red line) that corresponds to the standard criterion for statistical significance, p = .05 (two-tailed). This shows that published results are selected for significance. The dashed red line shows significance for p < .10, which is often used for marginal significance. Thus, there are more results that are presented as significant than the .05 criterion suggests.

3. To quantify the amount of selection bias, z-curve fits a statistical model to the distribution of statistically significant results (z > 1.96). The grey curve shows the predicted values for the observed significant results and the unobserved non-significant results. The statistically significant results (including z > 6) make up 21% of the total area under the grey curve. This is called the expected discovery rate because the results provide an estimate of the percentage of significant results that researchers actually obtain in their statistical analyses. In comparison, the percentage of significant results (including z > 6) includes 78% of the published results. This percentage is called the observed discovery rate, which is the rate of significant results in published journal articles. The difference between a 78% ODR and a 21% EDR provides an estimate of the extent of selection for significance. The difference of nearly 60 percentage points is the largest difference observed for any department analyzed so far (k = 11). The upper level of the 95% confidence interval for the EDR is 34%. Thus, the discrepancy is not just random. To put this result in context, it is possible to compare it to the average for 120 psychology journals in 2010 (Schimmack, 2022). The ODR (78% vs. 72%) is higher and the EDR (21% vs. 28%) is lower, suggesting more severe selection for significance for research published by McGill faculty members included in this analysis.

4. The z-curve model also estimates the average power of the subset of studies with significant results (p < .05, two-tailed). This estimate is called the expected replication rate (ERR) because it predicts the percentage of significant results that are expected if the same analyses were repeated in exact replication studies with the same sample sizes. The ERR of 66% suggests a fairly high replication rate. The problem is that actual replication rates are lower than the ERR predictions (about 40% Open Science Collaboration, 2015). The main reason is that it is impossible to conduct exact replication studies and that selection for significance will lead to a regression to the mean when replication studies are not exact. Thus, the ERR represents the best case scenario that is unrealistic. In contrast, the EDR represents the worst case scenario in which selection for significance does not select more powerful studies and the success rate of replication studies is not different from the success rate of original studies. The EDR of 21% is lower than the actual replication success rate of 40%. To predict the success rate of actual replication studies, I am using the average of the EDR and ERR, which is called the actual replication prediction (ARP). For Columbia, the ARP is (66 + 21)/2 = 44%. This is close to the currently best estimate of the success rate for actual replication studies based on the Open Science Collaboration project (~40%). Thus, research from McGill University is expected to replicate at the average rate of actual replication studies.

5. The EDR can be used to estimate the risk that published results are false positives (i.e., a statistically significant result when H0 is true), using Soric’s (1989) formula for the maximum false discovery rate. An EDR of 21% implies that no more than 20% of the significant results are false positives, but the lower limit of the 95%CI of the EDR, 12%, allows for 39% false positive results. Most readers are likely to agree that this is too high. One solution to this problem is to lower the conventional criterion for statistical significance (Benjamin et al., 2017). Figure 2 shows that alpha = .005 reduces the point estimate of the FDR to 3% with an upper limit of the 95% confidence interval of 9%. Thus, without any further information readers could use this criterion to interpret results published in articles by psychology researchers at Columbia. Of course, this criterion will be inappropriate for some researchers, but the present results show that the traditional alpha criterion of .05 is also inappropriate to maintain a reasonably low probability of false positive results.

Some researchers have changed research practices in response to the replication crisis. It is therefore interesting to examine whether replicability of newer research has improved. To examine this question, I performed a z-curve analysis for articles published in the past five year (2016-2021).

The results are disappointing. The point estimate, 18%, is even lower than for all year, 21%, although the difference could just be sampling error. Mostly, these results suggest that the psychology department at McGill University has not responded to the replication crisis in psychology, despite a low replication rate that provides more room for improvement. It will be interesting to see whether the large cohort of assistant professors adopted better research practices and will boost McGill’s standing in the replicability rankings of psychology departments.

There is considerable variability across individual researchers, although confidence intervals are often wide due to the smaller number of test statistics. The table below shows the meta-statistics of all faculty members that provided results for the departmental z-curve. You can see the z-curve for individual faculty member by clicking on their name.

Rank	Name	ARP	EDR	ERR	FDR
1	Caroline Palmer	71	75	68	2
2	Kristine H. Onishi	60	69	51	5
3	Melanie A. Dirks	54	78	31	12
4	Richard Koestner	50	67	32	11
5	Yitzchak M. Binik	49	73	25	16
6	John E. Lydon	44	61	28	14
7	Jelena Ristic	44	69	18	24
8	Mark W. Baldwin	43	54	33	11
9	Jennifer A. Bartz	39	58	19	22
10	Blaine Ditto	17	27	7	67

Since 2011, it is an open secret that many published results in psychology journals do not replicate. The replicability of published results is particularly low in social psychology (Open Science Collaboration, 2015).

A key reason for low replicability is that researchers are rewarded for publishing as many articles as possible without concerns about the replicability of the published findings. This incentive structure is maintained by journal editors, review panels of granting agencies, and hiring and promotion committees at universities.

To change the incentive structure, I developed the Replicability Index, a blog that critically examined the replicability, credibility, and integrity of psychological science. In 2016, I created the first replicability rankings of psychology departments (Schimmack, 2016). Based on scientific criticisms of these methods, I have improved the selection process of articles to be used in departmental reviews.

1. I am using Web of Science to obtain lists of published articles from individual authors (Schimmack, 2022). This method minimizes the chance that articles that do not belong to an author are included in a replicability analysis. It also allows me to classify researchers into areas based on the frequency of publications in specialized journals. Currently, I cannot evaluate neuroscience research. So, the rankings are limited to cognitive, social, developmental, clinical, and applied psychologists.

2. I am using department’s websites to identify researchers that belong to the psychology department. This eliminates articles that are from other departments.

3. I am only using tenured, active professors. This eliminates emeritus professors from the evaluation of departments. I am not including assistant professors because the published results might negatively impact their chances to get tenure. Another reason is that they often do not have enough publications at their current university to produce meaningful results.

Like all empirical research, the present results rely on a number of assumptions and have some limitations. The main limitations are that
(a) only results that were found in an automatic search are included
(b) only results published in 120 journals are included (see list of journals)
(c) published significant results (p < .05) may not be a representative sample of all significant results
(d) point estimates are imprecise and can vary based on sampling error alone.

These limitations do not invalidate the results. Large difference in replicability estimates are likely to predict real differences in success rates of actual replication studies (Schimmack, 2022).

Princeton University

I used the department website to find core members of the psychology department. I found 24 professors and 4 associate professors. I used Web of Science to download references related to the authors name and initial. An r-script searched for related publications in the database of publications in 120 psychology journals.

Not all researchers conduct quantitative research and report test statistics in their result sections. Therefore, the analysis is limited to 17 faculty members that had at least 100 test statistics. This criterion eliminated many faculty members who publish predominantly in neuroscience journals.

Figure 1 shows the z-curve for all 6,199 tests statistics. I use the Figure to explain how a z-curve analysis provides information about replicability and other useful meta-statistics.

1. All test-statistics are converted into absolute z-scores as a common metric of the strength of evidence (effect size over sampling error) against the null-hypothesis (typically H0 = no effect). A z-curve plot is a histogram of absolute z-scores in the range from 0 to 6. The 710 z-scores greater than 6 are not shown because z-scores of this magnitude are extremely unlikely to occur when the null-hypothesis is true (particle physics uses z > 5 for significance). Although they are not shown, they are included in the computation of the meta-statistics.

2. Visual inspection of the histogram shows a steep drop in frequencies at z = 1.96 (solid red line) that corresponds to the standard criterion for statistical significance, p = .05 (two-tailed). This shows that published results are selected for significance. The dashed red line shows significance for p < .10, which is often used for marginal significance. Thus, there are more results that are presented as significant than the .05 criterion suggests.

3. To quantify the amount of selection bias, z-curve fits a statistical model to the distribution of statistically significant results (z > 1.96). The grey curve shows the predicted values for the observed significant results and the unobserved non-significant results. The statistically significant results (including z > 6) make up 40% of the total area under the grey curve. This is called the expected discovery rate because the results provide an estimate of the percentage of significant results that researchers actually obtain in their statistical analyses. In comparison, the percentage of significant results (including z > 6) includes 70% of the published results. This percentage is called the observed discovery rate, which is the rate of significant results in published journal articles. The difference between a 70% ODR and a 401% EDR provides an estimate of the extent of selection for significance. The difference of~ 30 percentage points is large, but one of the smallest difference for investigations of psychology departments. The upper level of the 95% confidence interval for the EDR is 51%. Thus, the discrepancy is not just random. To put this result in context, it is possible to compare it to the average for 120 psychology journals in 2010 (Schimmack, 2022). The ODR (70% vs. 72%) is similar, but the EDR is higher (40% vs. 28%). Although this difference is not statistically significant, it suggests that the typical study at Princeton has slightly more power than studies in psychology in general.

4. The z-curve model also estimates the average power of the subset of studies with significant results (p < .05, two-tailed). This estimate is called the expected replication rate (ERR) because it predicts the percentage of significant results that are expected if the same analyses were repeated in exact replication studies with the same sample sizes. The ERR of 65% suggests a fairly high replication rate. The problem is that actual replication rates are lower than the ERR predictions (about 40% Open Science Collaboration, 2015). The main reason is that it is impossible to conduct exact replication studies and that selection for significance will lead to a regression to the mean when replication studies are not exact. Thus, the ERR represents the best case scenario that is unrealistic. In contrast, the EDR represents the worst case scenario in which selection for significance does not select more powerful studies and the success rate of replication studies is not different from the success rate of original studies. To predict the success rate of actual replication studies, I am using the average of the EDR and ERR, which is called the actual replication prediction (ARP). For Princeton, the ARP is (65 + 40)/2 = 52.5%. This is somewhat higher than the currently best estimate of the success rate for actual replication studies based on the Open Science Collaboration project (~40%). Thus, research from Columbia University is expected to replicate at a slightly higher rate than studies in psychology in general.

5. The EDR can be used to estimate the risk that published results are false positives (i.e., a statistically significant result when H0 is true), using Soric’s (1989) formula for the maximum false discovery rate. An EDR of 40% implies that no more than 8% of the significant results are false positives, but the lower limit of the 95%CI of the EDR, 31%, allows for 12% false positive results. To lower the risk of a false positive result, it is possible to reduce the significance threshold to alpha = .005 (Benjamin et al., 2017). Figure 2 shows that implications of this new criterion (z = 2.8). The false positive risk is now 2% and even the upper limit of the 95% confidence interval is only 3%. Thus, without any further information readers could use this criterion to interpret results published in articles by psychology researchers at Princeton.

Some researchers have changed research practices in response to the replication crisis. It is therefore interesting to examine whether replicability of newer research has improved. To examine this question, I performed a z-curve analysis for articles published in the past five year (2016-2021).

The point estimate of the EDR increased from 40% to 61%, but due to the relatively small number of observations this change is not statistically significant. It is also problematic that z-curve plot shows a higher frequency of z-scores between 2.2 and 2.4 rather than 2.0 and 2.2. While there are many reasons for this finding, one explanation could be that some researchers use a new criterion value for selection. Rather than publishing any p-value below .05, they may only publish p-values below .02, for example. This practice would bias the z-curve estimates that assume no further selection effects once a p-value is below .05.

The next figure shows the results for an analysis that excludes z-scores between 2 and 2.2 from the analysis. The main finding is that the EDR estimate drops from 61% to 25%. As a result, the FDR estimate increases from 3% to 16%. Thus, it is too early to conclude that Princeton’s research has become notably more replicable, and I would personally continue to use alpha = .005 to reject null-hypotheses.

10 of the 17 faculty members with useful data were classified as social psychologists. The following analysis is limited to the z-scores of these 10 faculty members to examine whether social psychological research is less replicable (Open Science Collaboration, 2015).

The EDR is slightly, but not significantly, lower, but still higher than the EDR of other departments. Thus, there is no evidence to suggest that social psychology at Princeton is less replicable than research in other areas. Other areas did not have sufficient test statistics for a meaningful analysis.

There is considerable variability across individual researchers, although confidence intervals are often wide due to the smaller number of test statistics. The table below shows the meta-statistics of all faculty members that provided results for the departmental z-curve. You can see the z-curve for individual faculty member by clicking on their name.

Rank	Name	ARP	EDR	ERR	FDR
1	Uri Hasson	82	83	81	1
2	Kenneth A. Norman	73	75	71	2
3	Jordan A. Taylor	68	77	60	4
4	Elke U. Weber	66	70	63	3
5	Tania Lombrozo	65	73	58	4
6	Diana I. Tamir	59	69	50	5
7	Yael Niv	58	68	47	6
8	Emily Pronin	51	68	34	10
9	Jonathan D. Cohen	50	76	23	17
10	Alin Coman	49	57	40	8
11	Molly J. Crockett	49	75	23	17
12	J. Nicole Shelton	47	55	39	8
13	Susan T. Fiske	46	70	22	19
14	Stacey Sinclair	40	49	31	12
15	Eldar Shafir	35	55	14	31
16	Deborah A. Prentice	33	55	11	44
17	Joel Cooper	28	44	12	39