Category Archives: Multi-Method

Open Communication about the invalidity of the race IAT

In the old days, most scientific communication occured behind closed doors, when reviewers provide anonymous peer-reviews that determine the fate of manuscripts. In the old days, rejected manuscripts would not be able to contribute to scientific communications because nobody would know about them.

All of this has changed with the birth of open science. Now authors can share manuscripts on pre-print servers and researchers can discuss merits of these manuscripts on social media. The benefit of this open scientific communication is that more people can join in and contribute to the communication.

Yoav Bar-Anan co-authored an article with Brian Nosek titled “Scientific Utopia: I. Opening Scientific Communication.” In this spirit of openness, I would like to have an open scientific communication with Yoav and his co-author Michelangelo Vianello about their 2018 article “A Multi-Method Multi-Trait Test of the Dual-Attitude Perspective

I have criticized their model in an in press article in Perspectives of Psychological Science (Schimmack, 2019). In a commentary, Yoav and Michelangelo argue that their model is “compatible with the logic of an MTMM investigation (Campbell & Fiske, 1959). They argue that it is important to have multiple traits to identify method variance in a matrix with multiple measures of multiple traits. They then propose that I lost the ability to identify method variance by examining one attitude (i.e., race, self-esteem, political orientation) at a time. They then point out that I did not include all measures and included the Modern Racism Scale as an indicator of political orientation to note that I did not provide a reason for these choices. While this is true, Yoav and Michelangelo had access to the data and could have tested whether these choices made any differences. They do not. This is obvious for the modern racism scale that can be eliminated from the measurement model without any changes in the overall model.

To cut to the chase, the main source of disagreement is the modelling of method variance in the multi-trait-multi-method data set. The issue is clear when we examine the original model published in Bar-Anan and Vianello (2018).

In this model, method variance in IATs and related tasks like the Brief IAT is modelled with the INDIRECT METHOD factor. The model assumes that all of the method variance that is present in implicit measures is shared across attitude domains and across all implicit measures. The only way for this model to allow for different amounts of method variance in different implicit measures is by assigning different loadings to the various methods. Moreover, the loadings provide information about the nature of the shared variance and the amount of method variance in the various methods. Although this is valuable and important information, the authors never discuss this information and its implications.

Many of these loadings are very small. For example, the loading of the race IAT and the brief race IAT are .11 and .02. In other words, the correlation between these two measures is inflated by .11 * .02 = .0022 points. This means that the correlation of r = .52 between these two measures is r = .5178 after we remove the influence of method variance.

It makes absolutely no sense to accuse me of separating the models, when there is no evidence of implicit method variance that is shared across attitudes. The remaining parameter estimates are not affected if a factor with low loadings is removed from a model.

Here I show that examining one attitude at a time produces exactly the same results as the full model. I focus on the most controversial IAT; the race IAT. After all, there is general agreement that there is little evidence of discriminant validity for political orientation (r = .91, in the Figure above), and there is little evidence for any validity in the self-esteem IAT based on several other investigations of this topic with a multi-method approach (Bosson et al., 2000; Falk et al., 2015).

Model 1 is based on Yoav and Michelangelo’s model that assumes that there is practically no method variance in IAT-variants. Thus, we can fit a simple dual-attitude model to the data. In this model, contact is regressed onto implicit and explicit attitude factors to see the unique contribution of the two factors without making causal assumptions. The model has acceptable fit, CFI = .952, RMSEA = .013.

The correlation between the two factors is .66, while it is r = .69 in the full model in Figure 1. The loading of the race IAT on the implicit factor is .66, while it is .62 in the full model in Figure 1. Thus, as expected based on the low loadings on the IMPLICIT METHOD factor, the results are no different when the model is fitted only to the measure of racial attitudes.

Model 2 makes the assumption that IAT-variants share method variance. Adding the method factor to the model increased model fit, CFI = .973, RMSEA = .010. As the models are nested, it is also possible to compare model fit with a chi-square test. With five degrees of freedom difference, chi-square changed from 167. 19 to 112.32. Thus, the model comparison favours the model with a method factor.

The main difference between the models is that there the evidence is less supportive of a dual attitude model and that the amount of valid variance in the race IAT decreases from .66^2 = 43% to r = .47^2 = 22%.

In sum, the 2018 article made strong claims about the race IAT. These claims were based on a model that implied that there is no systematic measurement error in IAT scores. I showed that this assumption is false and that a model with a method factor for IATs and IAT-variants fits the data better than a model without such a factor. It also makes no theoretical sense to postulate that there is no systematic method variance in IATs, when several previous studies have demonstrated that attitudes are only one source of variance in IAT scores (Klauer, Voss, Schmitz, & Teige-Mocigemba, 2007).

How is it possible that the race IAT and other IATs are widely used in psychological research and on public websites to provide individuals with false feedback about their hidden attitudes without any evidence of its validity as an individual difference measure of hidden attitudes that influence behaviour outside of awareness?

The answer is that most of these studies assumed that the IAT is valid rather than testing its validity. Another reason is that psychological research is focused on providing evidence that confirms theories rather than subjecting theories to empirical tests that they may fail. Finally, psychologists ignore effect sizes. As a result, the finding that IAT scores have incremental predictive validity of less than 4% variance in a criterion is celebrated as evidence for the validity of IATs, but even this small estimate is based on underpowered studies and may shrink in replication studies (cf. Kurdi et al., 2019).

It is understandable that proponents of the IAT respond with defiant defensiveness to my critique of the IAT. However, I am not the first to question the validity of the IAT, but these criticisms were ignored. At least Banaji and Greenwald recognized in 2013 that they do “not have the luxury of believing that what appears true and valid now will always appear so” (p. xv). It is time to face the facts. It may be painful to accept that the IAT is not what it was promised to be 21 years ago, but that is what the current evidence suggests. There is nothing wrong with my models and their interpretation, and it is time to tell visitors of the Project Implicit website that they should not attach any meaning to their IAT scores. A more productive way to counter my criticism of the IAT would be to conduct a proper validation study with multiple methods and validation criteria that are predicted to be uniquely related to IAT scores in a preregistered study.

References

Bosson, J. K., Swann, W. B., Jr., & Pennebaker, J. W. (2000). Stalking the perfect measure of implicit self-esteem: The blind men and the elephant revisited? Journal of Personality and Social Psychology, 79, 631–643.

Falk, C. F., Heine, S. J., Takemura, K., Zhang, C. X., & Hsu, C. (2015). Are implicit self-esteem measures valid for assessing individual and cultural differences. Journal of Personality, 83, 56–68. doi:10.1111/jopy.12082

Klauer, K. C., Voss, A., Schmitz, F., & Teige-Mocigemba, S. (2007). Process components of the Implicit Association Test: A diffusion-model analysis. Journal of Personality and Social Psychology, 93, 353–368.

Kurdi, B., Seitchik, A. E., Axt, J. R., Carroll, T. J., Karapetyan, A., Kaushik, N., . . . Banaji, M. R. (2019). Relationship between the Implicit Association Test and intergroup behavior: A meta-analysis. American Psychologist, 74, 569–586.

The Validation Crisis in Psychology

Most published psychological measures are unvalid.  (subtitle)
*unvalid = the validity of the measure is un-known.

This blog post served as a first draft for a manuscript that is currently under review at Meta-Psychology. You can find the latest version here (pdf).

Introduction

8 years ago, psychologists started to realize that they have a replication crisis. Many published results do not replicate in honest replication attempts that allow the data to decide whether a hypothesis is true or false.

The replication crisis is sometimes attributed to the lack of replication studies before 2011. However, this is not the case. Most published results were replicated successfully. However, these successes were entirely predictable from the fact that only successful replications would be published (Sterling, 1959). These sham replication studies provided illusory evidence for theories that have been discredited over the past eight years by credible replication studies.

New initiatives that are called open science are likely to improve the replicability of psychological science in the future, although progress towards this goal is painfully slow.

This blog post addresses another problem in psychological science. I call it the validation crisis. Replicability is only one necessary feature of a healthy science. Another necessary feature of a healthy science is the use of valid measures. This feature of a healthy science is as obvious as the need for replicability. To test theories that relate theoretical constructs to each other (e.g., construct A influences construct B for individuals drawn from population P under conditions C), it is necessary to have valid measures of constructs. However, it is unclear which criteria a measure has to fulfill to have construct validity. Thus, even successful and replicable tests of a theory may be false because the measures that were used lacked construct validity.

Construct Validity

The classic article on “Construct Validity” was written by two giants in psychology; Cronbach and Meehl (1955). Every graduate student of psychology and surely every psychologists who published a psychological measure should be familiar with this article.

The article was the result of an APA task force that tried to establish criteria, now called psychometric properties, for tests to be published. The result of this project was the creation of the construct “Construct validity”

The chief innovation in the Committee’s report was the term construct validity. (p. 281).

Cronbach and Meehl provide their own definition of this construct.

Construct validation is involved whenever a test is to be interpreted
as a measure of some attribute or quality which is not “operationally
defined” (p. 282).

In modern language, construct validity is the relationship between variation in observed test scores and a latent variable that reflects corresponding variation in a theoretical construct (Schimmack, 2010).

Thinking about construct validity in this way makes it immediately obvious why it is much easier to demonstrate predictive validity, which is the relationship between observed tests scores and observed criterion scores than to establish construct validity, which is the relationship between observed test scores and a latent, unobserved variable. To demonstrate predictive validity, one can simply obtain scores on a measure and a criterion and compute the correlation between the two variables. The correlation coefficient shows the amount of predictive validity of the measure. However, because constructs are not observable, it is impossible to use simple correlations to examine construct validity.

The problem of construct validation can be illustrated with the development of IQ scores. IQ scores can have predictive validity (e.g., performance in graduate school) without making any claims about the construct that is being measured (IQ tests measure whatever they measure and what they measure predicts important outcomes). However, IQ tests are often treated as measures of intelligence. For IQ tests to be valid measures of intelligence, it is necessary to define the construct of intelligence and to demonstrate that observed IQ scores are related to unobserved variation in intelligence. Thus, construct validation requires clear definitions of constructs that are independent of the measure that is being validated. Without clear definition of constructs, the meaning of a measure reverts essentially to “whatever the measure is measuring,” as in the old saying “Intelligence is whatever IQ tests are measuring. This saying shows the problem of research with measures that have no clear construct and no construct validity.

In conclusion, the challenge in construct validation research is to relate a specific measure to a well-defined construct and to establish that variation in test scores are related to variation in the construct.

What are Constructs

Construct validation starts with an assumption. Individuals are assumed to have an attribute, today we may say personality trait. Personality traits are typically not directly observable (e.g., kindness rather than height), but systematic observation suggests that the attribute exists (some people are kinder than others across time and situations). The first step is to develop a measure of this attribute (e.g., a self-report measure “How kind are you?”). If the test is valid, variation in the observed scores on the measure should be related to the personality trait.

A construct is some postulated attribute of people, assumed to be reflected in test performance (p. 283).

The term “reflected” is consistent with a latent variable model, where unobserved traits are reflected in observable indicators. In fact, Cronbach and Meehl argue that factor analysis (not principle component analysis!) provides very important information for construct validity.

We depart from Anastasi at two points. She writes, “The validity of
a psychological test should not be confused with an analysis of the factors
which determine the behavior under consideration.” We, however,
regard such analysis as a most important type of validation. (p. 286).

Factor analysis is useful because factors are unobserved variables and factor loadings show how strongly an observed measure is related to variation in a an unobserved variable; the factor. If multiple measures of a construct are available, they should be positively correlated with each other and factor analysis will extract a common factor. For example, if multiple independent raters agree in their ratings of individuals’ kindness, the common factor in these ratings may correspond to the personality trait kindness, and the factor loadings provide evidence about the degree of construct validity of each measure (Schimmack, 2010).

In conclusion, factor analysis provides useful information about construct validity of measures because factors represent the construct and factor loadings show how strongly an observed measure is related to the construct.

It is clear that factors here function as constructs (p. 287).

Convergent Validity

The term convergent validity was introduced a few years later in another seminal article on validation research by Campbell and Fiske (1959). However, the basic idea of convergent validity was specified by Cronbach and Meehl (1955) in the section “Correlation matrices and factor analysis”

If two tests are presumed to measure the same construct, a correlation between them is predicted (p. 287).

If a trait such as dominance is hypothesized, and the items inquire about behaviors subsumed under this label, then the hypothesis appears to require that these items be generally intercorrelated (p. 288)

Cronbach and Meehl realize the problem of using just two observed measures to examine convergent validity. For example, self-informant correlations are often used in personality psychology to demonstrate validity of self-ratings. However, a correlation of r = .4 between self-ratings and informant ratings is open to very different interpretations. The correlation could reflect very high validity of self-ratings and modest validity of informant ratings or the opposite could be true.

If the obtained correlation departs from the expectation, however, there is no way to know whether the fault lies in test A, test B, or the formulation of the construct. A matrix of intercorrelations often points out profitable ways of dividing the construct into more meaningful parts, factor analysis being
a useful computational method in such studies. (p. 300)

A multi-method approach avoids this problem and factor loadings on a common factor can be interpreted as validity coefficients. More valid measures should have higher loadings than less valid measures. Factor analysis requires a minimum of three observed variables, but more is better. Thus, construct validation requires a multi-method assessment.

Discriminant Validity

The term discriminant validity was also introduced later by Campbell and Fiske (1959). However, Cronbach and Meehl already point out that high or low correlations can support construct validity. Crucial for construct validity is that the correlations are consistent with theoretical expectations.

For example, low correlations between intelligence and happiness do not undermine the validity of an intelligence measure because there is no theoretical expectation that intelligence is related to happiness. In contrast, low correlations between intelligence and job performance would be a problem if the jobs require problem solving skills and intelligence is an ability to solve problems faster or better.

Only if the underlying theory of the trait being measured calls for high item
intercorrelations do the correlations support construct validity (p. 288).

Quantifying Construct Validity

It is rare to see quantitative claims about construct validity. Most articles that claim construct validity of a measure simply state that the measure has demonstrated construct validity as if a test is either valid or invalid. However, the previous discussion already made it clear that construct validity is a quantitative construct because construct validity is the relation between variation in a measure and variation in the construct and this relation can vary . If we use standardized coefficients like factor loadings to assess the construct validity of a measure, construct validity can range from -1 to 1.

Contrary to the current practices, Cronbach and Meehl assumed that most users of measures would be interested in a “construct validity coefficient.”

There is an understandable tendency to seek a “construct validity
coefficient. A numerical statement of the degree of construct validity
would be a statement of the proportion of the test score variance that is
attributable to the construct variable. This numerical estimate can sometimes be arrived at by a factor analysis” (p. 289).

Cronbach and Meehl are well-aware that it is difficult to quantify validity precisely, even if multiple measures of a construct are available because the factor may not be perfectly corresponding with the construct.

Rarely will it be possible to estimate definite “construct saturations,” because no factor corresponding closely to the construct will be available (p. 289).

And nobody today seems to remember Cronbach and Meehl’s (1955) warning that rejection of the null-hypothesis, the test has zero validity, is not the end goal of validation research.

It should be particularly noted that rejecting the null hypothesis does not finish the job of construct validation (p. 290)

The problem is not to conclude that the test “is valid” for measuring- the construct variable. The task is to state as definitely as possible the degree of validity the test is presumed to have (p. 290).

One reason why psychologists may not follow this sensible advice is that estimates of construct validity for many tests are likely to be low (Schimmack, 2010).

The Nomological Net – A Structural Equation Model

Some readers may be familiar with the term “nomological net” that was popularized by Cronbach and Meehl. In modern language a nomological net is essentially a structural equation model.

The laws in a nomological network may relate (a) observable properties
or quantities to each other; or (b) theoretical constructs to observables;
or (c) different theoretical constructs to one another. These “laws”
may be statistical or deterministic.

It is probably no accident that at the same time as Cronbach and Mehl started to think about constructs as separate from observed measures, structural equation model was developed as a combination of factor analysis that made it possible to relate observed variables to variation in unobserved constructs and path analysis that made it possible to relate variation in constructs to each other. Although laws in a nomological network can take on more complex forms than linear relationships, a structural equation model is a nomological network (but a nomological network is not necessarily a structural equation model).

As proper construct validation requires a multi-method approach and demonstration of convergent and discriminant validity, SEM is ideally suited to examine whether the observed correlations among measures in a mulit-trait-multi-method matrix are consistent with theoretical expectations. In this regard, SEM is superior to factor analysis. For example, it is possible to model shared method variance, which is impossible with factor analysis.

Cronbach and Meehl also realize that constructs can change as more information becomes available. It may also occur that the data fail to provide evidence for a construct. In this sense, construct validiation is an ongoing process of improved understanding of unobserved constructs and how they are related to observable measures.

Ideally this iterative process would start with a simple structural equation model that is fitted to some data. If the model does not fit, the model can be modified and tested with new data. Over time, the model would become more complex and more stable because core measures of constructs would establish the construct validity, while peripheral relationships may be modified if new data suggest that theoretical assumptions need to be changed.

When observations will not fit into the network as it stands, the scientist has a certain freedom in selecting where to modify the network (p. 290).

Too often psychologists use SEM only to confirm an assumed nomological network and it is often considered inappropriate to change a nomological network to fit observed data. However, SEM is as much testing of an existing construct as exploration of a new construct.

The example from the natural sciences was the initial definition of gold as having a golden color. However, later it was discovered that the pure metal gold is actually silver or white and that the typical yellow color comes from copper impurities. In the same way, scientific constructs of intelligence can change depending on the data that are observed. For example, the original theory may assume that intelligence is a unidimensional construct (g), but empirical data could show that intelligence is multi-faceted with specific intelligences for specific domains.

However, given the lack of construct validation research in psychology, psychology has seen little progress in the understanding of such basic constructs such as extraversion, self-esteem, or wellbeing. Often these constructs are still assessed with measures that were originally proposed as measures of these constructs, as if divine intervention led to the creation of the best measure of these constructs and future research only confirmed their superiority.

Instead many claims about construct validity are based on conjectures than empirical support by means of nomological networks. This was true in 1955. Unfortunately, it is still true over 50 years later.

For most tests intended to measure constructs, adequate criteria do not exist. This being the case, many such tests have been left unvalidated, or a finespun network of rationalizations has been offered as if it were validation. Rationalization is not construct validation. One who claims that his test reflects a construct cannot maintain his claim in the face of recurrent negative results because these results show that his construct is too loosely defined to yield verifiable inferences (p. 291).

Given the difficulty of defining constructs and finding measures for it, even measures that show promise in the beginning might fail to demonstrate construct validity later and new measures should show higher construct validity than the early measures. However, psychology shows no development in measures of the same construct. The most widely used measure of self-esteem is still Rosenberg’s scale from 1965 and the most widely used measure of wellbieng is still Diener et al.’s scale from 1984. It is not clear how psychology can make progress, if it doesn’t make progress in the development of nomological networks that provide information about constructs and about the construct validity of measures.

Cronbach and Meehl are clear that nomological networks are needed to claim construct validity.

To validate a claim that a test measures a construct, a nomological net surrounding the concept must exist (p. 291).

However, there are few attempts to examine construct validity with structural equation models (Connelly & Ones, 2010; Zou, Schimmack, & Gere, 2013). [please share more if you know some]

One possible reason is that construct validation research may reveal that authors initial constructs need to be modified or their measures have modest validity. For example, McCrae, Zonderman, Costa, Bond, and Paunonen (1996) dismissed structural equation modeling as a useful method to examine the construct validity of Big Five measures because it failed to support their conception of the Big Five as orthogonal dimensions with simple structure.

Recommendations for Users of Psychological Measures

The consumer can accept a test as a measure of a construct only when there is a strong positive fit between predictions and subsequent data. When the evidence from a proper investigation of a published test is essentially negative, it should be reported as a stop sign to discourage use of the test pending a reconciliation of test and construct, or final abandonment of the test (p. 296).

It is very unlikely that all hunches by psychologists lead to the discovery of useful constructs and development of valid tests of these constructs. Given the lack of knowledge about the mind, it is rather more likely that many constructs turn out to be non-existent and that measures have low construct validity.

However, the history of psychological measurement has only seen development of more and more constructs and more and more measures to measure this increasing universe of constructs. Since the 1990s, constructs have doubled because every construct has been split into an explicit and an implicit version of the construct. Presumably, there is even implicit political orientation or gender identity.

The proliferation of constructs and measures is not a sign of a healthy science. Rather it shows the inability of empirical studies to demonstrate that a measure is not valid or that a construct may not exist. This is mostly due to self-serving biases and motivated reasoning of test developers. The gains from a measure that is widely used are immense. Thus, weak evidence is used to claim that a measure is valid and consumers are complicit because they can use these measures to make new discoveries. Even when evidence shows that a measure may not work as intended (e.g.,
Bosson et al., 2000), it is often ignored (Greenwald & Farnham, 2001).

Conclusion

Just like psychologist have started to appreciate replication failures in the past years, they need to embrace validation failures. Some of the measures that are currently used in psychology are likely to have insufficient construct validity. If this was the decade of replication, the 2020s may become the decade of validation, and maybe the 2030s may produce the first replicable studies with valid measures. Maybe this is overly optimistic, given the lack of improvement in validation research since Cronbach and Meehl (1955) outlined a program of construct validation research. Ample citations show that they were successful in introducing the term, but they failed in establishing rigorous criteria of construct validity. The time to change this is now.

A Quantitative Science Needs to Quantify Validity

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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