Category Archives: Convergent Validity

Racial Bias as a Trait

Construct Validation, Construct Validity, Convergent Validity, Implicit Association Test, Latent-Trait-State, race IAT

Prejudice is an important topic in psychology that can be examined from various perspectives. Nevertheless, prejudice research is typically studied by social psychologists. As a result, research has focused on social cognitive processes that are activated in response to racial stimuli (e.g., pictures of African Americans) and experimental manipulations of the situation (e.g., race of experimenter). Other research has focused on cognitive processes that can lead to the formation of racial bias (e.g., the minimal group paradigm). Sometimes this work has been based on a model of prejudice that assumes racial bias is a common attribute of all people (Devine, 1989) and that individuals only differ in their willingness or ability to act on their racial biases.

An alternative view is that racial biases vary across individuals and are shaped by experiences with out-group members. The most prominent theory is contact theory, which postulates that contact with out-group members reduces racial bias. In social psychology, individual differences in racial biases are typically called attitudes, where attitudes are broad dispositions to respond to a class of attitude objects in a consistent manner. For example, individuals with positive attitudes towards African Americans are more likely to have positive thoughts, feelings, and behaviors in interactions with African Americans.

The notion of attitudes as general dispositions shows that attitudes play the same role in social psychology that traits play in personality psychology. For example, extraversion is a general disposition to have more positive thoughts, feelings, and to engage more in social interactions. One important research question in personality psychology are the causes of variation in personality. Why are some people more extraverted than others? A related question is how stable personality traits are. If the causes of extraversion are environmental factors, extraversion should change when the environment changes. If the causes of extraversion are within the person (e.g., early childhood experiences, genetic differences), extraversion should be stable. Thus, the stability of personality traits over time is an empirical question that can only be answered in longitudinal studies that measure personality traits repeatedly. A meta-analysis shows that the Big Five personality traits are highly stable over time (Anusic & Schimmack, 2016).

In comparison, the stability of attitudes has received relatively little attention in social psychology because stable individual differences are often neglected in social cognitive models of attitudes. This is unfortunate because the origins of racial bias are important to the understanding of racial bias and to design interventions that help individuals to reduce their racial biases.

How stable are racial biases?

The lack of data has not stopped social psychologists from speculating about the stability of racial biases. “It’s not as malleable as mood and not as reliable as a personality trait. It’s in between the two–a blend of both a trait and a state characteristic” (Nosek in Azar, 2008). In 2019, Nosek was less certain about the stability of racial biases. “One is does that mean we have have some degree of trait variance because there is some stability over time and what is the rest? Is the rest error or is it state variance in some way, right. Some variation that is meaningful variation that is sensitive to the context of measurement. Surely it is some of both, but we don’t know how much” (The Psychology Podcast, 2019).

Other social psychologists have made stronger claims about the stability of racial bias. Payne argued that racial bias is a state because implicit bias measures show higher internal consistency than retest correlations (Payne, 2017). However, the comparison of internal consistency and retest correlations is problematic because situational factors may simply produce situation-specific measurement errors rather than reflecting real changes in the underlying trait; a problem that is well recognized in personality psychology. To examine this question more thoroughly, it is necessary to obtain multiple retests and decompose the variances into trait, state, and error variances (Anusic & Schimmack, 2016). Even this approach cannot distinguish between state variance and systematic measurement error, which requires multi-method data (Schimmack, 2019).

A Longitudinal Multi-Method Study of Racial Bias

A recent article reported the results of an impressive longitudinal study of racial bias with over 3,000 medical students who completed measures of racial bias and inter-group contact three times over a period of six year (first year of medical school, fourth year of medical school, 2nd year of residency) (Onyeador et al., 2019). I used the openly shared data to fit a multi-method state-trait-error model to the data (https://osf.io/78cqx/).

The model integrates several theoretical assumptions that are consistent with previous research (Schimmack, 2019). First, the model assumes that explicit ratings of racial bias (feeling thermometer) and implicit measures of racial bias (Implicit Association Test) are complementary measures of individual differences in racial bias. Second, the model assumes that one source of variance in racial bias is a stable trait. Third, the model assumes that racial bias differs across racial groups, in that Black individuals have more favorable attitudes towards Black people than members from other groups. Fourth, the model assumes that contact is negatively correlated with racial bias without making a strong causal assumption about the direction of this relationship. The model also assumes that Black individuals have more contact with Black individuals and that contact partially explains why Black individuals have less racial biases.

The new hypotheses that could be explored with these data concerned the presence of state variance in racial bias. First, state variance should produce correlations between the occasion specific variances of the two methods. That is, after statistically removing trait variance, residual state variance in feeling thermometer scores should be correlated with residual variances in IAT scores. For example, as medical students interact more with Black staff and patients in residency, their racial biases could change and this would produce changes in explicit ratings and in IAT scores. Second, state variance is expected to be somewhat stable over shorter time intervals because environments tend to be stable over shorter time intervals.

The model in Figure 1 met standard criteria of model fit, CFI = .997, RMSEA = .016.

Describing the model from left to right, race (0 = Black, 1 = White) has the expected relationship with quantity of contact (quant1) in year 1 (reflecting everyday interactions with Black individuals) and with the racial bias (att) factor. In addition, more contact is related to less pro-White bias (-.28). The attitude factor is a stronger predictor of the explicit trait factor (.78; ft; White feeling-thermometer – Black feeling-thermometer) than on the implicit trait factor (.60, iat). The influence of the explicit trait factor on measures on the three occasions (.58-.63) suggests that about one-third of the variance in these measures is trait variance. The same is true for individual IATs (.59-.62). The effect of the attitude factor on individual IATs (.60 * .60 = .36; .36^2 = .13 suggests that less than 20% of the variance in an individual IAT reflects racial bias. This estimate is consistent with the results from multi-method studies (Schimmack, 2019). However, these results suggests that the amount of valid trait variance can increase up to 36%, by aggregating scores of several IATs. In sum, these results provide first evidence that racial bias is stable over a period of six years and that both explicit ratings and implicit ratings capture trait variance in racial bias.

Turning to the bottom part of the model, there is weak evidence to suggest that residual variances (that are not trait variance) in explicit and implicit ratings are correlated. Although the correlation of r = .06 at time 1 is statistically significant, the correlations at time 2 (r = .03) and time 3 (r = .00) are not. This finding suggests that most of the residual variance is method specific measurement error rather than state-variance in racial bias. There is some evidence that the explicit ratings capture more than occasion-specific measurement error because state variance at time 1 predicts state variance at time 2 (r = .25) and from time 2 to time 3 (r = .20). This is not the case for the IAT scores. Finally, contact with Black medical staff at time 2 is a weak, but significant predictor of explicit measures of racial bias at time 2 and time 3, but it does not predict IAT scores at time 2 and 3. These findings do not support the hypothesis that changes in racial bias measures reflect real changes in racial biases.

The results are consistent with the only other multi-method longitudinal study of racial bias that covered only a brief period of three months. In this study, even implicit measures showed no convergent validity for the state (non-trait) variance on the same occasion (Cunningham, Preacher, & Banaji, 1995).

Conclusion

Examining predictors of individual differences in racial bias is important to understand the origins of racial biases and to develop interventions that help individuals to reduce their racial biases. Examining the stability of racial bias in longitudinal studies shows that these biases are stable dispositions and there is little evidence that they change with changing life-experiences. One explanation is that only close contact may be able to shift attitudes and that few people have close relationships with outgroup members. Thus stable environments may contribute to stability in racial bias.

Given the trait-like nature of racial bias, interventions that target attitudes and general dispositions may be relatively ineffective, as Onyeador et al.’s (2019) article suggested. Thus, it may be more effective to target and assess actual behaviors in diversity training. Expecting diversity training to change general dispositions may be misguided and lead to false conclusions about the effectiveness of diversity training programs.

The Implicit Association Test: A Measure in Search of a Construct (in press, PoPS)

Construct Validation, Construct Validity, Convergent Validity, Discriminant Validity, Implicit Association Test, Percentage of Valid Variance, race IAT, validation crisis, Validity, Validity Coefficient

Here is a link to the manuscript, data, and MPLUS scripts for reproducibility. https://osf.io/mu7e6/

ABSTRACT

Greenwald et al. (1998) proposed that the IAT measures individual differences in implicit social cognition.  This claim requires evidence of construct validity. I review the evidence and show that there is insufficient evidence for this claim.  Most important, I show that few studies were able to test discriminant validity of the IAT as a measure of implicit constructs. I examine discriminant validity in several multi-method studies and find no or weak evidence for discriminant validity. I also show that validity of the IAT as a measure of attitudes varies across constructs. Validity of the self-esteem IAT is low, but estimates vary across studies.  About 20% of the variance in the race IAT reflects racial preferences. The highest validity is obtained for measuring political orientation with the IAT (64% valid variance).  Most of this valid variance stems from a distinction between individuals with opposing attitudes, while reaction times contribute less than 10% of variance in the prediction of explicit attitude measures.  In all domains, explicit measures are more valid than the IAT, but the IAT can be used as a measure of sensitive attitudes to reduce measurement error by using a multi-method measurement model.

Keywords:  Personality, Individual Differences, Social Cognition, Measurement, Construct Validity, Convergent Validity, Discriminant Validity, Structural Equation Modeling

HIGHLIGHTS

Despite its popularity, relatively little is known about the construct validity of the IAT.

As Cronbach (1989) pointed out, construct validation is better examined by independent experts than by authors of a test because “colleagues are especially able to refine the interpretation, as they compensate for blind spots and capitalize on their own distinctive experience” (p. 163).

It is of utmost importance to determine how much of the variance in IAT scores is valid variance and how much of the variance is due to measurement error, especially when IAT scores are used to provide individualized feedback.

There is also no consensus in the literature whether the IAT measures something different from explicit measures.

In conclusion, while there is general consensus to make a distinction between explicit measures and implicit measures, it is not clear what the IAT measures

To complicate matters further, the validity of the IAT may vary across attitude objects. After all the IAT is a method, just like Likert scales are a method, and it is impossible to say that a method is valid (Cronbach, 1971).

At present, relatively little is known about the contribution of these three parameters to observed correlations in hundreds of mono-method studies.

A Critical Review of Greenwald et al.’s (1998) Original Article

In conclusion, the seminal IAT article introduced the IAT as a measure of implicit constructs that cannot be measured with explicit measures, but it did not really test this dual-attitude model.

Construct Validity in 2007

In conclusion, the 2007 review of construct validity revealed major psychometric challenges for the construct validity of the IAT, which explains why some researchers have concluded that the IAT cannot be used to measure individual differences (Payne et al., 2017).  It also revealed that most studies were mono-method studies that could not examine convergent and discriminant validity

Cunningham, Preacher and Banaji (2001)

Another noteworthy finding is that a single factor accounted for correlations among all measures on the same occasion and across measurement occasions. This finding shows that there were no true changes in racial attitudes over the course of this two-month study.  This finding is important because Cunningham et al.’s (2001) study is often cited as evidence that implicit attitudes are highly unstable and malleable (e.g., Payne et al., 2017). This interpretation is based on the failure to distinguish random measurement error and true change in the construct that is being measured (Anusic & Schimmack, 2016).  While Cunningham et al.’s (2001) results suggest that the IAT is a highly unreliable measure, the results also suggest that the racial attitudes that are measured with the race IAT are highly stable over periods of weeks or months. 

Bar-Anan & Vianello, 2018

this large study of construct validity also provides little evidence for the original claim that the IAT measures a new construct that cannot be measured with explicit measures, and confirms the estimate from Cunningham et al. (2001) that about 20% of the variance in IAT scores reflects variance in racial attitudes.

Greenwald et al. (2009)

“When entered after the self-report measures, the two implicit measures incrementally explained 2.1% of vote intention variance, p=.001, and when political conservativism was also included in the model, “the pair of implicit measures incrementally predicted only 0.6% of voting intention variance, p = .05.”  (Greenwald et al., 2009, p. 247).

I tried to reproduce these results with the published correlation matrix and failed to do so. I contacted Anthony Greenwald, who provided the raw data, but I was unable to recreate the sample size of N = 1,057. Instead I obtained a similar sample size of N = 1,035.  Performing the analysis on this sample also produced non-significant results (IAT: b = -.003, se = .044, t = .070, p = .944; AMP: b = -.014, se = .042, t = 0.344, p = .731).  Thus, there is no evidence for incremental predictive validity in this study.

Axt (2018)

With N = 540,723 respondents, sampling error is very small, σ = .002, and parameter estimates can be interpreted as true scores in the population of Project Implicit visitors.  A comparison of the factor loadings shows that explicit ratings are more valid than IAT scores. The factor loading of the race IAT on the attitude factor once more suggests that about 20% of the variance in IAT scores reflects racial attitudes

Falk, Heine, Zhang, and Hsu (2015)

Most important, the self-esteem IAT and the other implicit measures have low and non-significant loadings on the self-esteem factor. 

Bar-Anan & Vianello (2018)

Thus, low validity contributes considerably to low observed correlations between IAT scores and explicit self-esteem measures.

Bar-Anan & Vianello (2018) – Political Orientation

More important, the factor loading of the IAT on the implicit factor is much higher than for self-esteem or racial attitudes, suggesting over 50% of the variance in political orientation IAT scores is valid variance, π = .79, σ = .016.  The loading of the self-report on the explicit ratings was also higher, π = .90, σ = .010

Variation of Implicit – Explicit Correlations Across Domains

This suggests that the IAT is good in classifying individuals into opposing groups, but it has low validity of individual differences in the strength of attitudes.

What Do IATs Measure?

The present results suggest that measurement error alone is often sufficient to explain these low correlations.  Thus, there is little empirical support for the claim that the IAT measures implicit attitudes that are not accessible to introspection and that cannot be measured with self-report measures. 

For 21 years the lack of discriminant validity has been overlooked because psychologists often fail to take measurement error into account and do not clearly distinguish between measures and constructs.

In the future, researchers need to be more careful when they make claims about constructs based on a single measure like the IAT because measurement error can produce misleading results.

Researchers should avoid terms like implicit attitude or implicit preferences that make claims about constructs simply because attitudes were measured with an implicit measure

Recently, Greenwald and Banaji (2017) also expressed concerns about their earlier assumption that IAT scores reflect unconscious processes.  “Even though the present authors find themselves occasionally lapsing to use implicit and explicit as if they had conceptual meaning, they strongly endorse the empirical understanding of the implicit– explicit distinction” (p. 862).

How Well Does the IAT Measure What it Measures?

Studies with the IAT can be divided into applied studies (A-studies) and basic studies (B-studies).  B-studies employ the IAT to study basic psychological processes.  In contrast, A-studies use the IAT as a measure of individual differences. Whereas B-studies contribute to the understanding of the IAT, A-studies require that IAT scores have construct validity.  Thus, B-studies should provide quantitative information about the psychometric properties for researchers who are conducting A-studies. Unfortunately, 21 years of B-studies have failed to do so. For example, after an exhaustive review of the IAT literature, de Houwer et al. (2009) conclude that “IAT effects are reliable enough to be used as a measure of individual differences” (p. 363).  This conclusion is not helpful for the use of the IAT in A-studies because (a) no quantitative information about reliability is given, and (b) reliability is necessary but not sufficient for validity.  Height can be measured reliably, but it is not a valid measure of happiness. 

This article provides the first quantitative information about validity of three IATs.  The evidence suggests that the self-esteem IAT has no clear evidence of construct validity (Falk et al., 2015).  The race-IAT has about 20% valid variance and even less valid variance in studies that focus on attitudes of members from a single group.  The political orientation IAT has over 40% valid variance, but most of this variance is explained by group-differences and overlaps with explicit measures of political orientation.  Although validity of the IAT needs to be examined on a case by case basis, the results suggest that the IAT has limited utility as a measurement method in A-studies.  It is either invalid or the construct can be measured more easily with direct ratings.

Implications for the Use of IAT scores in Personality Assessment

I suggest to replace the reliability coefficient with the validity coefficient.  For example, if we assume that 20% of the variance in scores on the race IAT is valid variance, the 95%CI for IAT scores from Project Implicit (Axt, 2018), using the D-scoring method, with a mean of .30 and a standard deviation of.46 ranges from -.51 to 1.11. Thus, participants who score at the mean level could have an extreme pro-White bias (Cohen’s d = 1.11/.46 = 2.41), but also an extreme pro-Black Bias (Cohen’s d = -.51/.46 = -1.10).  Thus, it seems problematic to provide individuals with feedback that their IAT score may reveal something about their attitudes that is more valid than their beliefs. 

Conclusion

Social psychologists have always distrusted self-report, especially for the measurement of sensitive topics like prejudice.  Many attempts were made to measure attitudes and other constructs with indirect methods.  The IAT was a major breakthrough because it has relatively high reliability compared to other methods.  Thus, creating the IAT was a major achievement that should not be underestimated because the IAT lacks construct validity as a measure of implicit constructs. Even creating an indirect measure of attitudes is a formidable feat. However, in the early 1990s, social psychologists were enthralled by work in cognitive psychology that demonstrated unconscious or uncontrollable processes (Greenwald & Banaji, 1995). Implicit measures were based on this work and it seemed reasonable to assume that they might provide a window into the unconscious (Banaji & Greenwald, 2013). However, the processes that are involved in the measurement of attitudes with implicit measures are not the personality characteristics that are being measured.  There is nothing implicit about being a Republican or Democrat, gay or straight, or having low self-esteem.  Conflating implicit processes in the measurement of attitudes with implicit personality constructs has created a lot of confusion. It is time to end this confusion. The IAT is an implicit measure of attitudes with varying validity.  It is not a window into people’s unconscious feelings, cognitions, or attitudes.

A Quantitative Science Needs to Quantify Validity

Campbell & Fiske, Convergent Validity, MTMM, Multi-Method, Percentage of Valid Variance, Validity, Validity Coefficient

Background

This article was published in a special issue in the European Journal of Personality Psychology.   It examines the unresolved issue of validating psychological measures fro the perspective of a multi-method approach (Campbell & Fiske, 1959), using structural equation modeling.

I think it provides a reasonable alternative to the current interest in modeling residual variance in personality questionnaires (network perspective) and solves the problems of manifest personality measures that are confounded by systematic measurement error.

Although latent variable models of multi-method data have been used in structural analyses (Biesanz & West, 2004; deYoung, 2006), these studies have rarely been used to estimate validity of personality measures.  This article shows how this can be done and what assumptions need to be made to interpret latent factors as variance in true personality traits.

Hopefully, sharing this article openly on this blog can generated some discussion about the future of personality measurement in psychology.

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What Multi-Method Data Tell Us About
Construct Validity
ULRICH SCHIMMACK*
University of Toronto Mississauga, Canada

European Journal of Personality
Eur. J. Pers. 24: 241–257 (2010)
DOI: 10.1002/per.771  [for original article]

Abstract

Structural equation modelling of multi-method data has become a popular method to
examine construct validity and to control for random and systematic measurement error in personality measures. I review the essential assumptions underlying causal models of
multi-method data and their implications for estimating the validity of personality
measures. The main conclusions are that causal models of multi-method data can be
used to obtain quantitative estimates of the amount of valid variance in measures of
personality dispositions, but that it is more difficult to determine the validity of personality measures of act frequencies and situation-specific dispositions.

Key words: statistical methods; personality scales and inventories; regression methods;
history of psychology; construct validity; causal modelling; multi-method; measurement

INTRODUCTION

Fifty years ago, Campbell and Fiske (1959) published the groundbreaking article
Convergent and Discriminant Validation by the Multitrait-Multimethod Matrix.With close to 5000 citations (Web of Science, February 1, 2010), it is the most cited article in
Psychological Bulletin. The major contribution of this article was to outline an empirical
procedure for testing the validity of personality measures. It is difficult to overestimate the importance of this contribution because it is impossible to test personality theories
empirically without valid measures of personality.

Despite its high citation count, Campbell and Fiske’s work is often neglected in
introductory textbooks, presumably because validation is considered to be an obscure and complicated process (Borsboom, 2006). Undergraduate students of personality psychology learn little more than the definition of a valid measure as a measure that measures what it is supposed to measure.

However, they are not taught how personality psychologists validate their measures. One might hope that aspiring personality researchers learn about Campbell and Fiske’s multi-method approach during graduate school. Unfortunately, even handbooks dedicated to research methods in personality psychology pay relatively little attention to Campbell and Fiske’s (1959) seminal contribution (John & Soto, 2007; Simms & Watson, 2007). More importantly, construct validity is often introduced in qualitative terms.

In contrast, when Cronbach and Meehl (1955) introduced the concept of construct validity, they proposed a quantitative definition of construct validity as the proportion of construct-related variance in the observed variance of a personality measure. Although the authors noted that it would be difficult to obtain precise estimates of construct validity coefficients (CVCs), they stressed the importance of estimating ‘as definitely as possible the degree of validity the test is presumed to have’ (p. 290).

Campbell and Fiske’s (1959) multi-method approach paved the way to do so. Although Campbell and Fiske’s article examined construct validity qualitatively, subsequent developments in psychometrics allowed researchers to obtain quantitative estimates of construct validity based on causal models of multi-method data (Eid, Lischetzke, Nussbeck, & Trierweiler, 2003; Kenny & Kashy, 1992). Research articles in leading personality journals routinely report these estimates (Biesanz & West, 2004; DeYoung, 2006; Diener, Smith, & Fujita, 1995), but a systematic and accessible introduction to causal models of multi-method data is lacking.

The main purpose of this paper is to explain how causal models of multi-method data can be used to obtain quantitative estimates of construct validity and which assumptions these models make to yield accurate estimates.

I prefer the term causal model to the more commonly used term structural equation model because I interpret latent variables in these models as unobserved, yet real causal forces that produce variation in observed measures (Borsboom, Mellenbergh,&
van Heerden, 2003). I make the case below that this realistic interpretation of latent factors is necessary to use multi-method data for construct validation research because the assumption of causality is crucial for the identification of latent variables with construct variance (CV).

Campbell and Fiske (1959) distinguished absolute and relative (construct) validity. To
examine relative construct validity it is necessary to measure multiple traits and to look for evidence of convergent and discriminant validity in a multi-trait-multi-method matrix (Simms &Watson, 2007). However, to examine construct validity in an absolute sense, it is only necessary to measure one construct with multiple methods.

In this paper, I focus on convergent validity across multiple measures of a single construct because causal models of multi-method data rely on convergent validity alone to examine construct validity.

As discussed in more detail below, causal models of multi-method data estimate
construct validity quantitatively with the factor loadings of observed personality measures on a latent factor (i.e. an unobserved variable) that represents the valid variance of a construct. The amount of valid variance in a personality measure can be obtained by squaring its factor loading on this latent factor. In this paper, I use the terms construct validity coefficient (CVC) to refer to the factor loading and the term construct variance (CV) for the amount of valid variance in a personality measure.

Validity

A measure is valid if it measures what it was designed to measure. For example, a
thermometer is a valid measure of temperature in part because the recorded values covary with humans’ sensory perceptions of temperature (Cronbach & Meehl, 1955). A modern thermometer is a more valid measure of temperature than humans’ sensory perceptions, but the correlation between scores on a thermometer and humans’ sensory perceptions is necessary to demonstrate that a thermometer measures temperature. It would be odd to claim that highly reliable scores recorded by an expensive and complicated instrument measure temperature if these scores were unrelated to humans’ everyday perceptions of temperature.

The definition of validity as a property of a measure has important implications for
empirical tests of validity. Namely, researchers first need a clearly defined construct before they can validate a potential measure of the construct. For example, to evaluate a measure of anxiety researchers first need to define anxiety and then examine the validity of a measure as a measure of anxiety. Although the importance of clear definitions for construct validation research may seem obvious, validation research often seems to work in the opposite direction; that is, after a measure has been created psychologists examine what it measures.

For example, the widely used Positive Affect and Negative Affect Schedule (PANAS) has two scales named Positive Affect (PA) and Negative Affect (NA). These scales are based on exploratory factor analyses of mood ratings (Watson, Clark, & Tellegen, 1988). As a result, Positive Affect and Negative Affect are merely labels for the first two VARIMAX rotated principal components that emerged in these analyses. Thus, it is meaningless to examine whether the PANAS scales are valid measures of PA and NA. They are valid measures of PA and NA by definition because PA and NA are mere labels of the two VARIMAX rotated principal components that emerge in factor analyses of mood ratings.

A construct validation study would have to start with an a priori definition of Positive Affect and Negative Affect that does not refer to the specific measurement procedure that was used to create the PANAS scales. For example, some researchers have
defined Positive Affect and Negative Affect as the valence of affective experiences and
have pointed out problems of the PANAS scales as measures of pleasant and unpleasant
affective experiences (see Schimmack, 2007, for a review).

However, the authors of the PANAS do not view their measure as a measure of hedonic valence. To clarify their position, they proposed to change the labels of their scales from Positive Affect and Negative Affect to Positive Activation and Negative Activation (Watson,Wiese, Vaidya, & Tellegen, 1999). The willingness to change labels indicates that PANAS scales do not measure a priori defined constructs and as a result there is no criterion to evaluate the construct validity of the PANAS scales.

The previous example illustrates how personality measures assume a life of their own
and implicitly become the construct; that is, a construct is operationally defined by the
method that is used to measure it (Borsboom, 2006). A main contribution of Cambpell and Fiske’s (1959) article was to argue forcefully against operationalism and for a separation of constructs and methods. This separation is essential for validation research because validation research has to allow for the possibility that some of the observed variance is invalid.

Other sciences clearly follow this approach. For example, physics has clearly defined
concepts such as time or temperature. Over the past centuries, physicists have developed
increasingly precise ways of measuring these concepts, but the concepts have remained the same. Modern physics would be impossible without these advances in measurement.
However, psychologists do not follow this model of more advanced sciences. Typically, a
measure becomes popular and after it becomes popular it is equated with the construct. As a result, researchers continue to use old measure and rarely attempt to create better
measures of the same construct. Indeed, it is hard to find an example, in which one measure of a construct has replaced another measure of the same construct based on an empirical comparison of the construct validity of competing measures of the same construct (Grucza & Goldberg, 2007).

One reason for the lack of progress in the measurement of personality constructs could
be the belief that it is impossible to quantify the validity of a measure. If it were impossible to quantify the validity of a measure, then it also would be impossible to say which of two measures is more valid. However, causal models of multi-method data produce quantitative estimates of validity that allow comparisons of the validity of different measures.

One potential obstacle for construct validation research is the need to define
psychological constructs a priori without reference to empirical data. This can be difficult for constructs that make reference to cognitive processes (e.g. working memory capacity) or unconscious motives (implicit need for power). However, the need for a priori definitions is not a major problem in personality psychology. The reason is that everyday language provides thousands of relatively well-defined personality constructs (Allport & Odbert, 1936). In fact, all measures in personality psychology that are based on the lexical hypothesis assume that everyday concepts such as helpful or sociable are meaningful personality constructs. At least with regard to these relatively simple constructs, it is possible to test the construct validity of personality measures. For example, it is possible to examine whether a sociability scale really measures sociability and whether a measure of helpfulness really measures helpfulness.

Convergent validity

I start with a simple example to illustrate how psychologists can evaluate the validity of a
personality measure. The concept is people’s weight.Weight can be defined as ‘the vertical force exerted by a mass as a result of gravity’ (wordnet.princeton.edu). In the present case, only the mass of human adults is of interest. The main question, which has real practical significance in health psychology (Kroh, 2005), is to examine the validity of self-report measures of weight because it is more economical to use self-reports than to weigh people with scales.

To examine the validity of self-reported weight as a measure of actual weight, it is
possible to obtain self-reports of weight and an objective measure of weight from the same individuals. If self-reports of weight are valid, they should be highly correlated with the objective measure of weight. In one study, participants first reported their weight before their weight was objectively measured with a scale several weeks later (Rowland, 1990). The correlation in this study was r (N =11,284) =.98. The implications of this finding for the validity of self-reports of weight depend on the causal processes that underlie this correlation, which can be examined by means of causal modelling of correlational data.

It is well known that a simple correlation does not reveal the underlying causal process,
but that some causal process must explain why a correlation was observed (Chaplin, 2007). Broadly speaking, a correlation is determined by the strength of four causal effects, namely, the effect of observed variable A on observed variable B, the effect of observed variable B on observed variable A, and the effects of an unobserved variable C on observed variable A and on observed variable B.

In the present example, the observed variables are the self-reported weights and those recorded by a scale. To make inferences about the validity of self-reports of weight it is necessary to make assumptions about the causal processes that produce a correlation between these two methods. Fortunately, it is relatively easy to do so in this example. First, it is fairly certain that the values recorded by a scale are not influenced by individuals’ self-reports. No matter how much individuals insist that the scale is wrong, it will not change its score. Thus, it is clear that the causal effect of self-reports on
the objective measure is zero. It is also clear that self-reports of weight in this study were
not influenced by the objective measurement of weight in this study because self-reports
were obtained weeks before the actual weight was measured. Thus, the causal effect of the objectively recorded scores on self-rating is also zero. It follows that the correlation of r =.98 must have been produced by a causal effect of an unobserved third variable. A
plausible third variable is individuals’ actual mass. It is their actual mass that causes the
scale to record a higher or lower value and their actual mass also caused them to report a specific weight. The latter causal effect is probably mediated by prior objective
measurements with other scales, and the validity of these scales would influence the
validity of self-reports among other factors (e.g. socially desirable responding). In combination, the causal effects of actual mass on self-reports and on the scale produce the observed correlation of r =.98. This correlation is not sufficient to determine how strong the effects of weight on the two measures are. It is possible that the scale was a perfect measure of weight. In this case, the correlation between weight and the values recorded by the scale is 1. It follows, that the size of the effect of weight on self-reports of weight (or the factor loading of self-reported weight on the weight factor) has to be r =.98 to produce the observed correlation of r =.98 (1 *.98 = .98). In this case, the CVC of the self-report measure of weight would be .98. However, it is also possible that the scale is a slightly imperfect measure of weight. For example, participants may not have removed their shoes before stepping on the scale and differences in the weight of shoes (e.g. boots versus sandals) could have produced measurement error in the objective measure of individuals’ true weight. It is also possible that changes in weight over time reduce the validity of objective scores as a validation criterion for self-ratings several weeks earlier. In this case, the estimate underestimates the validity of self-ratings.

In the present context, the reasons for the lack of perfect convergent validity are irrelevant. The main point of this example was to illustrate how the correlation between two independent measures of the same construct can be used to obtain quantitative estimates of the validity of a personality measure. In this example, a conservative estimate of the CVC of self-reported weight as a measure of weight is .98 and the estimated amount of CVin the self-report measure is 96% (.98^2 = .96).
The example of self-reported weight was used to establish four important points about
construct validity. First, the example shows that convergent validity is sufficient to examine construct validity. The question of how self-reports of weight are related to measures of other constructs (e.g. height, social desirable responding) can be useful to examine sources of measurement error, but correlations with measures of other constructs are not needed to estimate CVCs. Second, empirical tests of construct validity do not have to be an endless process without clear results (Borsboom, 2006). At least for some self-report measures it is possible to provide a meaningful answer to the question of their validity. Third, validity is a quantitative construct. Qualitative conclusions that a measure is valid because validity is not zero (CVC>0, p<.05) or that a measure is invalid because validity is not perfect (CVC<1.0, p<.05) are not very helpful because most measures are valid and invalid (0<CVC<1). As a result, qualitative reviews of validity studies are often the source of fruitless controversies (Schimmack & Oishi, 2005). The validity of personality measures should be estimated quantitatively like other psychometric properties such as reliability coefficients, which are routinely reported in research articles (Schmidt & Hunter, 1996).

Validity is more important than reliability because reliable and invalid measures are
potentially more dangerous than unreliable measures (Blanton & Jaccard, 2006). Moreover, it is possible that a less reliable measure is more valid than a more reliable measure if the latter measure is more strongly contaminated by systematic measurement error (John & Soto, 2007). A likely explanation for the emphasis on reliability is the common tendency to equate constructs with measures. If a construct is equated with a measure, only random error can undermine the validity of a measure. The main contribution of Campbell and Fiske (1959) was to point out that systematic measurement error can also threaten the validity of personality measures. As a result, high reliability is insufficient evidence for the validity of a personality measure (Borsboom & Mellenbergh, 2002).

The third point illustrated in this example is that tests of convergent validity require
independent measures. Campbell and Fiske (1959) emphasized the importance of
independent measures when they defined convergent validity as the correlation between ‘maximally different methods’ (p. 83). In a causal model of multi-method data the independence assumption implies that the only causal effects that produce a correlation between two measures of the same construct are the causal effect of the construct on the two measures. This assumption implies that all the other potential causal effects that can produce correlations among observed measures have an effect size of zero. If this assumption is correct, the shared variance across independent methods represents CV. It is then possible to estimate the proportion of the shared variance relative to the total observed variance of a personality measure as an estimate of the amount of CV in this measure. For example, in the previous example I assumed that actual mass was the only causal force that contributed to the correlation between self-reports of weight and objective scale scores. This assumption would be violated if self-ratings were based on previous measurements with objective scales (which is likely) and objective scales share method variance that does not reflect actual weight (which is unlikely). Thus, even validation studies with objective measures implicitly make assumptions about the causal model underling these correlations.

In sum, the weight example illustrated how a causal model of the convergent validity
between two measures of the same construct can be used to obtain quantitative estimates of the construct validity of a self-report measure of a personality characteristic. The following example shows how the same approach can be used to examine the construct validity of measures that aim to assess personality traits without the help of an objective measure that relies on well-established measurement procedures for physical characteristics like weight.

CONVERGENT VALIDITY OF PERSONALITY MEASURES

A Hypothetical Example

I use helpfulness as an example. Helpfulness is relatively easy to define as ‘providing
assistance or serving a useful function’ (wordnetweb.princeton.edu/perl/webwn). Helpful can be used to describe a single act or an individual. If helpful is used to describe a single act, helpful is not only a characteristic of a person because helping behaviour is also influenced by situational factors and interactions between personality and situational factors. Thus, it is still necessary to provide a clearer definition of helpfulness as a personality characteristic before it is possible to examine the validity of a personality measure of helpfulness.

Personality psychologists use trait concepts like helpful in two different ways. The most
common approach is to define helpful as an internal disposition. This definition implies
causality. There are some causal factors within an individual that make it more likely for
this individual to act in a helpful manner than other individuals. The alternative approach is to define helpfulness as the frequency with which individuals act in a helpful manner. An individual is helpful if he or she acted in a helpful manner more often than other people. This approach is known as the act frequency approach. The broader theoretical differences between these two approaches are well known and have been discussed elsewhere (Block, 1989; Funder, 1991; McCrae & Costa, 1995). However, the implications of these two definitions of personality traits for the interpretation of multi-method data have not been discussed. Ironically, it is easier to examine the validity of personality measures that aim to assess internal dispositions that are not directly observable than to do so for personality measures that aim to assess frequencies of observable acts. This is ironic because intuitively it seems to be easier to count the frequency of observable acts than to measure unobservable internal dispositions. In fact, not too long ago some psychologists doubted that internal dispositions even exist (cf. Goldberg, 1992).

The measurement problem of the act frequency approach is that it is quite difficult to
observe individuals’ actual behaviours in the real world. For example, it is no trivial task to establish how often John was helpful in the past month. In comparison it is relatively easy to use correlations among multiple imperfect measures of observable behaviours to make inferences about the influence of unobserved internal dispositions on behaviour.

Figure 1. Theoretical model of multi-method data. Note. T = trait (general disposition); AF-c, AF-f, AF-s  = act frequencies with colleague, friend and spouse; S-c, S-f, S-s =situational and person x situation interaction effects on act frequencies; R-c, R-f, R-s = reports by colleague, friend and spouse; E-c, E-f, E-s =errors in reports by
colleague, friend and spouse.

Figure 1 illustrates how a causal model of multi-method data can be used for this purpose. In Figure 1, an unobserved general disposition to be helpful influences three observed measures of helpfulness. In this example, the three observed measures are informant ratings of helpfulness by a friend, a co-worker and a spouse. Unlike actual informant ratings in personality research, informants in this hypothetical example are only asked to report how often the target helped them in the past month. According to Figure 1, each informant report is influenced by two independent factors, namely, the actual frequency of helpful acts towards the informant and (systematic and random) measurement error in the reported frequencies of helpful acts towards the informant. The actual frequency of helpful acts is also influenced by two independent factors. One factor represents the general disposition to be helpful that influences helpful behaviours across situations. The other factor represents situational factors and person-situation interaction effects. To fully estimate all coefficients in this model (i.e. effect sizes of the postulated causal effects), it would be necessary to separate measurement error and valid variance in act frequencies.

This is impossible if, as in Figure 1, each act frequency is measured with a single method,
namely, one informant report. In contrast, the influence of the general disposition is
reflected in all three informant reports. As a result, it is possible to separate the variance due to the general disposition from all other variance components such as random error,
systematic rating biases, situation effects and personsituation interaction effects. It is
then possible to determine the validity of informant ratings as measures of the general
disposition, but it is impossible to (precisely) estimate the validity of informant ratings as
measures of act frequencies because the model cannot distinguish reporting errors from
situational influences on helping behaviour.

The causal model in Figure 1 makes numerous independence assumptions that specify
Campbell and Fiske’s (1959) requirement that traits should be assessed with independent
methods. First, the model assumes that biases in ratings by one rater are independent of
biases in ratings by other raters. Second, it assumes that situational factors and
person by situation interaction effects that influence helping one informant are independent of the situational and personsituation factors that influence helping other informants. Third, it assumes that rating biases are independent of situation and person by situation interaction effects for the same rater and across raters. Finally, it assumes that rating biases and situation effects are independent of the global disposition. In total, this amounts to 21 independence assumptions (i.e. Figure 1 includes seven exogeneous variables, that is, variables that do not have an arrow pointing at them, which implies 21 (7×6/2) relationships that the model assumes to be zero). If these independence assumptions are correct, the correlations among the three informant ratings can be used to determine the variation in the unobserved personality disposition to be helpful with perfect validity. This variance can then be used like the objective measure of weight in the previous example as the validation criterion for personality measures of the general
disposition to be helpful (e.g. self-ratings of general helpfulness). In sum, Figure 1
illustrates that a specific pattern of correlations among independent measures of the same construct can be used to obtain precise estimates of the amount of valid variance in a single measure.

The main challenge for actual empirical studies is to ensure that the methods in a multi-method model fulfill the independence assumptions. The following examples demonstrate the importance of the neglected independence assumption for the correct interpretation of causal models of multi-method data. I also show how researchers can partially test the independence assumption if sufficient methods are available and how researchers can estimate the validity of personality measures that aggregate scores from independent methods. Before I proceed, I should clarify that strict independence of methods is unlikely, just like other null-hypotheses are likely to be false. However, small violations of the independence assumption will only introduce small biases in estimates of CVCs.

Example 1: Multiple response formats

The first example is a widely cited study of the relation between Positive Affect and
Negative Affect (Green, Goldman,&Salovey, 1993). I chose this paper because the authors
emphasized the importance of a multi-method approach for the measurement of affect,
while neglecting Campbell and Fiske’s requirement that the methods should be maximally different. A major problem for any empirical multi-method study is to find multiple independent measures of the same construct. The authors used four self-report measures with different response formats for this purpose. However, the variation of response formats can only be considered a multi-method study, if one assumes that responses on one response format are independent of responses on the other response formats so that correlations across response formats can only be explained by a common causal effect of actual momentary affective experiences on each response format. However, the validity of all self-report measures depends on the ability and willingness of respondents to report their experiences accurately. Violations of this basic assumption introduce shared method variance among self-ratings on different response formats. For example, socially desirable responding can inflate ratings of positive experiences across response formats. Thus, Green et al.’s (1993) study assumed rather than tested the validity of self-ratings of momentary affective experiences. At best, their study was able to examine the contribution of stylistic tendencies in the use of specific response formats to variance in mood ratings, but these effects are known to be small (Schimmack, Bockenholt, & Reisenzein, 2002). In sum, Green et al.’s (1993) article illustrates the importance of critically examining the similarity of methods in a multi-method study. Studies that use multiple self-report measures that vary response formats, scales, or measurement occasions should not be considered multi-method studies that can be used to examine construct validity.

Example 2: Three different measures

The second example of a multi-method study also examined the relation between Positive Affect and Negative Affect (Diener et al., 1995). However, it differs from the previous example in two important ways. First, the authors used more dissimilar methods that are less likely to violate the independence assumption, namely, self-report of affect in the past month, averaged daily affect ratings over a 6 week period and averaged ratings of general affect by multiple informants. Although these are different methods, it is possible that these methods are not strictly independent. For example, Diener et al. (1995) acknowledge that all three measures could be influenced by impression management. That is, retrospective and daily self-ratings could be influenced by social desirable responding, and informant ratings could be influenced by targets’ motivation to hide negative emotions from others. A common influence of impression management on all three methods would inflate validity estimates of all three methods.

For this paper, I used Diener et al.’s (1995) multi-method data to estimate CVCs for the
three methods as measures of general dispositions that influence people’s positive and
negative affective experiences. I used the data from Diener et al.’s (1995) Table 15 that are reproduced in Table 1. I used MPLUS5.1 for these analyses and all subsequent analyses (Muthen & Muthen, 2008). I fitted a simple model with a single latent variable that represents a general disposition that has causal effects on the three measures. Model fit was perfect because a model with three variables and three parameters has zero degrees of freedom and can perfectly reproduce the observed pattern of correlations. The perfect fit implies that CVC estimates are unbiased if the model assumptions are correct, but it also implies that the data are unable to test model assumptions.
These results suggest impressive validity of self-ratings of affect (Table 2). In contrast,
CVC estimates of informant ratings are considerably lower, despite the fact that informant ratings are based on averages of several informants. The non-overlapping confidence intervals for self-ratings and informant ratings indicate that this difference is statistically significant. There are two interpretations of this pattern. On the one hand, it is possible that informants are less knowledgeable about targets’ affective experiences. After all, they do not have access to information that is only available introspectively. However, this privileged information does not guarantee that self-ratings are more valid because individuals only have privileged information about their momentary feelings in specific situations rather than the internal dispositions that influence these feelings. On the other hand, it is possible that retrospective and daily self-ratings share method variance and do not fulfill the independence assumption. In this case, the causal model would provide inflated estimates of the validity of self-ratings because it assumes that stronger correlations between retrospective and daily self-ratings reveal higher validity of these methods, when in reality the higher correlation is caused by shared method effects. A study with three methods is unable to test these alternative explanations.

Example 3: Informants as multiple methods

One limitation of Diener et al.’s (1995) study was the aggregation of informant ratings.
Although aggregated informant ratings provide more valid information than ratings by a
single informant, the aggregation of informant ratings destroys valuable information about the correlations among informant ratings. The example in Figure 1 illustrated that ratings by multiple informants provide one of the easiest ways to measure dispositions with multiple methods because informants are more likely to base their ratings on different situations, which is necessary to reveal the influence of internal dispositions.

Example 3 shows how ratings by multiple informants can be used in construct validation research. The data for this example are based on multi-method data from the Riverside Accuracy Project (Funder, 1995; Schimmack, Oishi, Furr, & Funder, 2004). To make the CVC estimates comparable to those based on the previous example, I used scores on the depression and cheerfulness facets of the NEO-PI-R (Costa&McCrae, 1992). These facets are designed to measure affective dispositions. The multi-method model used self-ratings and informant ratings by parents, college friends and hometown friends as different methods.

Table 3 shows the correlation matrices for cheerfulness and depression. I first fitted a causal model that assumed independence of all methods to the data. The model also included sum scores of observed measures to examine the validity of aggregated informant ratings and an aggregated measure of all four raters (Figure 2). Model fit was evaluated using standard criteria of model fit, namely, comparative fit index (CFI)>.95, root mean square error of approximation (RMSEA)<.06 and standardized
root mean residuals (SRMR)<.08.

Neither cheerfulness, chi2 (df =2, N =222) = 11.30, p<.01, CFI =.860, RMSEA =.182, SRMR = .066, nor depression, chi2 (df =2, N = 222) = 8.31, p =.02,  CFI =. 915, RMSEA = .150, SRMR =.052, had acceptable CFI and RSMEA values.

One possible explanation for this finding is that self-ratings are not independent of informant ratings because self-ratings and informant ratings could be partially based on overlapping situations. For example, self-ratings of cheerfulness could be heavily influenced by the same situations that are also used by college friends to rate cheerfulness (e.g. parties). In this case, some of the agreement between self-ratings and informant ratings by college friends would reflect the specific situational factors of
overlapping situations, which leads to shared variance between these ratings that does not reflect the general disposition. In contrast, it is more likely that informant ratings are independent of each other because informants are less likely to rely on the same situations (Funder, 1995). For example, college friends may rely on different situations than parents.

To examine this possibility, I fitted a model that included additional relations between  self-ratings and informant ratings (dotted lines in Figure 2). For cheerfulness, an additional relation between self-ratings and ratings by college friends was sufficient to achieve acceptable model fit, chi2 (df =1, N =222) =0.08, p =.78, CFI =1.00, RMSEA =.000,
SRMR =.005. For depression, additional relations of self-ratings to ratings by college
friends and parents were necessary to achieve acceptable model fit. Model fit of this model was perfect because it has zero degrees of freedom. In these models, CVC can no longer be estimated by factor loadings alone because some of the valid variance in self-ratings is also shared with informant ratings. In this case, CVC estimates represent the combined total effect of the direct effect of the latent disposition factor on self-ratings and the indirect effects that are mediated by informant ratings.

I used the model indirect option of MPLUS5.1 to estimate the total effects in a model that  also included sum scores with equal weights for the three informant ratings and all four ratings.  Table 4 lists the CVC estimates for the four ratings and the two measures based on aggregated ratings.

The CVC estimates of self-ratings are considerably lower than those based on Diener
et al.’s (1995) data. Moreover, the results suggest that in this study aggregated informant
ratings are more valid than self-ratings, although the confidence intervals overlap. The
results for the aggregated measure of all four raters show that adding self-ratings to
informant ratings did not increase validity above and beyond the validity obtained by
aggregating informant ratings.

These results should not be taken too seriously because they are based on a single,
relatively small sample. Moreover, it is important to emphasize that these CVC estimates
depend on the assumption that informant ratings do not share method variance. Violation of this assumption would lead to an underestimation of the validity of self-ratings. For example, an alternative assumption would be that personality changes. As a result, parent ratings and ratings by hometown friends may share variance because they are based in part on situations before personality changed, whereas college friends’ ratings are based on more recent situations. This model fits the data equally well and leads to much higher estimates of CV in self-ratings. To test these competing models it would be necessary to include additional measures. For example, standardized laboratory tasks and biological measures could be added to the design to separate valid variance from shared rating biases by informants.

These inconsistent findings might suggest that it is futile to obtain wildly divergent quantitative estimates of construct validity. However, the same problem arises in other research areas and it can be addressed by designing better studies that test assumptions that cannot be tested in existing data sets. In fact, I believe that publication of conflicting validity estimates will stimulate research on construct validity, whereas the view of construct validation research as an obscure process without clear results has obscured the lack of knowledge about the validity of personality measures.

IMPLICATIONS

I used two multi-method datasets to illustrate how causal models of multi-method data can be used to estimate the validity of personality measures. The studies produced different results. It is not the purpose of this paper to examine the sources of disagreement. The results merely show that it is difficult to make general claims about the validity of commonly used personality measures. Until more precise information becomes available, the results suggest that about 30–70% of the variance in self-ratings and single informant ratings is CV. Until more precise estimates become available I suggest an estimate of 50 +/- 20% as a rough estimate of construct validity of personality ratings.

I suggest the verbal labels low validity for measures with less than 30% CV (e.g. implicit measures of well-being, Walker & Schimmack, 2008), moderate validity for measures with 30–70% CV (most self-report measures of personality traits) and high validity for measures with more than 70% CV (self-ratings of height and weight). Subsequently, I briefly discuss the practical implications of using self-report measures with moderate validity to study the causes and consequences of personality dispositions.

Correction for invalidity

Measurement error is nearly unavoidable, especially in the measurement of complex
constructs such as personality dispositions. Schmidt and Hunter (1996) provided
26 examples of how the failure to correct for measurement error can bias substantive
conclusions. One limitation of their important article was the focus on random
measurement error. The main reason is probably that information about random
measurement error is readily available. However, invalid variance due to systematic
measurement error is another factor that can distort research findings. Moreover, given
the moderate amount of valid variance in personality measures, corrections for invalidity are likely to have more dramatic practical implications than corrections for unreliability. The following examples illustrate this point.

Hundreds of twin studies have examined the similarity between MZ and DZ twins to
examine the heritability of personality characteristics. A common finding in these studies are moderate to large MZ correlations (r =.3–.5) and small to moderate (r =.1–.3) DZ correlations. This finding has led to the conclusion that approximately 40% of the variance is heritable and 60% of the variance is caused by environmental factors. However, this interpretation of twin data fails to take measurement error into account. As it turns out, MZ correlations approach, if not exceed, the amount of validity variance in personality measures as estimated by multi-method data. In other words, ratings by two different individuals of two different individuals (self-ratings by MZ twins) tend to correlate as highly with each other as those of a single individual (self ratings and informant ratings of a single target). This finding suggests that heritability estimates based on mono-method studies severely underestimate heritability of personality dispositions (Riemann, Angleitner, & Strelau, 1997). A correction for invalidity would suggest that most of the valid variance is heritable (Lykken&Tellegen, 1996). However, it is problematic to apply a direct correction for invalidity to twin data because this correction assumes that the independence assumption is valid. It is better to combine a multi-method assessment with a twin design (Riemann et al., 1997). It is also important to realize that multi-method models focus on internal dispositions rather than act frequencies. It makes sense that heritability estimates of internal dispositions are higher than heritability estimates of act frequencies because act frequencies are also influenced by situational factors.

Stability of personality dispositions

The study of stability of personality has a long history in personality psychology (Conley,
1984). However, empirical conclusions about the actual stability of personality are
hampered by the lack of good data. Most studies have relied on self-report data to examine this question. Given the moderate validity of self-ratings, it is likely that studies based on self-ratings underestimate true stability of personality. Even corrections for unreliability alone are sufficient to achieve impressive stability estimates of r =.98 over a 1-year interval (Anusic & Schimmack, 2016; Conley, 1984). The evidence for stability of personality from multi-method studies is even more impressive. For example, one study reported a retest correlation of r =.46 over a 26-year interval for a self-report measure of neuroticism (Conley, 1985). It seems possible that personality could change considerably over such a long time period. However, the study also included informant ratings of personality. Self-informant agreement on the same occasion was also r =.46. Under the assumption that self-ratings and informant ratings are independent methods and that there is no stability in method variance, this pattern of correlations would imply that variation in neuroticism did not change at all over this 26-year period (.46/.46 =1.00). However, this conclusion rests on the validity of the assumption that method variance is not stable. Given the availability of longitudinal multi-method data it is possible to test this assumption. The relevant information is contained in the cross-informant, cross-occasion correlations. If method  variance was unstable, these correlations should also be r =.46. In contrast, the actual correlations are lower, r =.32. This finding indicates that (a) personality dispositions changed and (b) there is some stability in the method variance. However, the actual stability of personality dispositions is still considerably higher (r =.32/.46 =.70) than one would have inferred from the observed retest correlation r =.46 of self-ratings alone. A retest correlation of r =.70 over a 26-year interval is consistent with other estimates that the stability of personality dispositions is about r =.90 over a 10-year period and r =.98 over a 1-year period (Conley, 1984; Terracciano, Costa, & McCrae, 2006) and that the majority of the variance is due to stable traits that never change (Anusic & Schimmack, 2016). The failure to realize
that observed retest correlations underestimate stability of personality dispositions can be costly because it gives personality researchers a false impression about the likelihood of finding empirical evidence for personality change. Given the true stability of personality it is necessary to wait a long time or to use large sample sizes and probably best to do both (Mroczek, 2007).

Prediction of behaviour and life outcomes

During the person-situation debate, it was proposed that a single personality trait predicts less than 10% of the variance in actual behaviours. However, most of these studies relied on self-ratings of personality to measure personality. Given the moderate validity of self-ratings, the observed correlation severely underestimates the actual effect of personality traits on behaviour. For example, a recent meta-analysis reported an effect size of conscientiousness on GPA of r =.24 (Noftle & Robins, 2007). Ozer (2007) points out
that strictly speaking the correlation between self-reported conscientiousness and GPA
does not represent the magnitude of a causal effect.

Assuming 40% valid variance in self-report measures of conscientiousness (DeYoung, 2006), the true effect size of a conscientious disposition on GPA is r =.38 (.24/sqrt(.40)). As a result, the amount of explained variance in GPA increases from 6% to 14%. Once more, failure to correct for invalidity in personality measures can be costly. For example, a personality researcher might identify seven causal factors that independently produce observed effect size estimates of r =.24, which suggests that these seven factors explain less than 50% of the variance in GPA (7 * .24^2 =42%). However, decades of future research are unable to uncover additional predictors of GPA. The reason could be that the true amount of explained variance is nearly 100% and that the unexplained variance is due to invalid variance in personality measures (7 * .38^2 =100%).

CONCLUSION

This paper provided an introduction to the logic of a multi-method study of construct
validity. I showed how causal models of multi-method data can be used to obtain
quantitative estimates of the construct validity of personality measures. I showed that
accurate estimates of construct validity depend on the validity of the assumptions
underlying a causal model of multi-method data such as the assumption that methods are independent. I also showed that multi-method studies of construct validity require
postulating a causal construct that can influence and produce covariances among
independent methods. Multi-method studies for other constructs such as actual behaviours or act frequencies are more problematic because act frequencies do not predict a specific pattern of correlations across methods. Finally, I presented some preliminary evidence that commonly used self-ratings of personality are likely to have a moderate amount of valid variance that falls broadly in a range from 30% to 70% of the total variance. This estimate is consistent with meta-analyses of self-informant agreement (Connolly, Kavanagh, & Viswesvaran, 2007; Schneider & Schimmack, 2009). However, the existing evidence is limited and more rigorous tests of construct validity are needed. Moreover studies with large, representative samples are needed to obtain more precise estimates of construct validity (Zou, Schimmack, & Gere, 2013). Hopefully, this paper will stimulate more research in this fundamental area of personality psychology by challenging the description of construct validity research as a Kafkaesque pursuit of an elusive goal that can never be reached (cf. Borsboom, 2006). Instead empirical studies of construct validity are a viable and important scientific enterprise that faces the same challenges as other studies in personality psychology that try
to make sense of correlational data.

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