This article has Open Peer Review reports available.
Should researchers use single indicators, best indicators, or multiple indicators in structural equation models?
© Hayduk and Littvay; licensee BioMed Central Ltd. 2012
Received: 9 June 2011
Accepted: 14 October 2012
Published: 22 October 2012
Structural equation modeling developed as a statistical melding of path analysis and factor analysis that obscured a fundamental tension between a factor preference for multiple indicators and path modeling’s openness to fewer indicators.
Multiple indicators hamper theory by unnecessarily restricting the number of modeled latents. Using the few best indicators – possibly even the single best indicator of each latent – encourages development of theoretically sophisticated models. Additional latent variables permit stronger statistical control of potential confounders, and encourage detailed investigation of mediating causal mechanisms.
We recommend the use of the few best indicators. One or two indicators are often sufficient, but three indicators may occasionally be helpful. More than three indicators are rarely warranted because additional redundant indicators provide less research benefit than single indicators of additional latent variables. Scales created from multiple indicators can introduce additional problems, and are prone to being less desirable than either single or multiple indicators.
Structural equation modeling melds path analysis and factor analysis under a common statistical framework. The multiple-indicator factor tradition includes works by Thurstone , Harman , Lawley & Maxwell , and Mulaik , while the single-indicator path tradition has roots in regression and includes Wright [5, 6], Blalock , Duncan , and Heise . Recent structural equation introductions range from having a heavy factor focus (Byrne ), through works seemly oblivious to path-factor tensions (Kline , Byrne [12, 13], Bollen ), to path oriented discussions (Hayduk [15, 16]). The path and factor approaches differ noticeably in regard to procedure, testing, and indicators.
In arguing against Anderson & Gerbing’s [17, 18] procedural suggestion to use a factor model before introducing latent paths, Fornell and Yi [19, 20] implicitly contrasted the path and factor approaches. Hayduk’s  additional critiques of the factor-model-before-path-model idea led to extensive SEMNET  discussions and a special issue of Structural Equation Modeling where a target article challenging the use of factor-models before latent path-models (Hayduk and Glaser ) was followed by commentaries (Mulaik and Millsap , Bollen , Bentler , Herting & Costner ), and a rejoinder (Hayduk and Glaser ). The weaknesses of the factor-model-first idea became painfully obvious, so subsequent SEMNET discussions switched to the topic of model testing – which again pitted the path-model inclined (who favored diagnostic attention to significant evidence of model ill-fit) against the factor-model inclined (who sought to replace model testing with indexing). This led to a special issue of Personality and Individual Differences in which Barrett’s  target article called for reporting and respecting the model χ2 test. Barrett’s call was neither strong nor precise enough for some (Hayduk, Cummings, Boadu, Pazderak-Robinson, & Boulianne , McIntosh ) but was “challenging” to those having factor analytic backgrounds (Millsap , Mulaik , Steiger ) – though the disarray among the dissenting replies signaled that careful model testing constitutes the new norm, even for factor models.
One additional path-versus-factor battle awaited, namely the matter of latents having single indicators (Hayduk & Pazderka-Robinson , Hayduk ). SEMNET again hosted multiple skirmishes, but it fell to the current article to organize the arguments regarding latents having relatively few indicators.
Organizing the issues
This model contains a strange conceptual bifurcation. The model claims considerable causal understanding in one model segment (the latents’ effects on the indicators) and complete causal ignorance in another segment (the saturated non-directional relationships among the latents). The researcher constructing this model did not fear causation itself because the model requires latent to indicator causal actions. It is more likely that the causal-segmentation arose from the complexity and difficulty of considering specific latent-to-latent causal connections. It is common to not know the latent level causal structure. But how should a structural equation modeler proceed when they don't know the latent causal structure?
What is required to move from a model like Figure 1 toward a Figure 2 model? One obvious, and difficult, concern is that any postulated latent-level effects should have worldly counterparts, and postulated absences of effects should correspond to worldly lacuna. A less obvious but important concern is that each latent variable participating in latent-to-latent causal effects must be identical to the latent acting causally toward specific indicators. This requirement actually provides substantial assistance, as we see shortly. We address the fixed measurement error variances depicted in Figure 2, later in this article. When we refer to measurement error variances, true scores, and the like, our concern is for validity via models that match the relevant worldly causal structures, rather than the mere reliability connotations such terms can carry in the context of classical test theory.
Consider a variable like η3 that is somewhere in the midst of the effects among the latents. η3's value (for any one case) is set by absorbing diversity (absorbing the potentially very different styles and magnitudes of effects arriving from η1, η2, and η3's error variable), and η3 emits the resultant value proportionately – namely in proportion to the magnitudes of the effects η3 emits. To specify such a causal nexus for η3 the researcher must theorize or understand η3 as being capable of the relevant absorptions and emissions – including η3's causal effects on its indicators.
Consider the causal connection between η3 and y5. The 1.0 effect depicted in Figure 2 does not make y5 a perfect reflection of η3 – it merely asserts a scale for η3 by asserting that each "perfect and isolated unit increase" (or decrease) in the true value of η3 (whether originating in η1, η2, or η3's error) would result in a corresponding unit increase (or decrease) in the indicator’s scaled value. This isolation and perfection is imaginary because a real unit change in latent η3 would mix with the measurement-error forces that also pummel the observed value of y5. The measurement error effects would nudge y5's value to be somewhat more or less than the perfect unit change originating in η3.
Error variances and latent meanings
The variance of the error-5 variable connected to y5 helps determine the meaning of the latent variable η3. If there were no causal variables influencing y5 other than η3, there would be no variance in the error-5 variable, and y5’s observed values would correspond exactly to, and have the same variance as, the true values of η3. Seeing y5’s values would directly report η3’s true values.
An opposite extreme occurs if the causal variables collectively referred to as y5’s error variable produce most of the variability in y5's values. Each real unit change in η3 still produces a corresponding unit for unit change in y5, but if the causal actions of the variables cumulated as y5’s error variable knock y5's values hither and yon, what is the identity of the η3 variable? η3 becomes any one of the many potential things that produces a minor amount of variation in y5's values. η3's identity is thrown into doubt because it becomes one (an unknown one) of the variables capable of producing some of y5’s variance.
Let us consider the more realistic case where η3 is neither perfectly reflected in y5's values, nor so minimally contributing to y5 that the researcher should consider discarding y5. The researcher presumably scaled η3 via the 1.0 effect to y5 because y5 was the best available indicator. For example, if y5 came from questionnaire data: the question providing y5 presumably was clear, precise and appropriately worded, there were few missing values, no recoding difficulties, no socially-desirable response, a reasonable distribution across multiple evenly-spaced response options, and so on. Being the best of the available indicators makes y5 unlikely to be almost all error, but it is also unlikely to be error-free.
Similarly, if η3A was the intended meaning for η3 in Figure 2, then all the “error” sources impinging upon the chain of indirect effects between η3A and y5 would constitute disruptive causal forces obscuring the true value of η3A. Hence, the error on y5 in Figure 2 would be the sum or accumulation of the causal features labeled error-B, error-C, and error-5 in Figure 3. While it is common to label disruptive causal forces connected to latents as residuals or structural-disturbances, and as measurement-errors if connected to indicators, we label all these as “errors” in Figure 3 because which specific disruptive causal forces constitute measurement-errors and which “residuals” remains open and requires careful researcher assessment.
The chain of effects leading through the three optional η3's to y5 warrants the use of y5 as an indicator of any one of η3A, η3B, or η3C, and the choice of which of these the researcher intends to incorporate in the latent level of the model dictates which causal actions constitute disruptions that should be accumulated into y5's error variable in Figure 2. The more extensive the disruptive forces, the larger the proportion of y5’s variance that is error but it is important to remember that the fundamental issue concerns the validity of the latent’s specification and not mere reliability.
Now we reverse the statements about error accumulation. By specifying the appropriate error-accumulation (the appropriate portion of y5’s variance) as fixed, the researcher could select whether the Figure 2 model contains η3C or η3B or η3A. To use η3C (in Figure 2) fix the variance of the error on y5 in Figure 2 to be the variance provided by only error-5. To select η3B, the variance on y5's error in Figure 2 should include variance produced by both error-5 and error-C in Figure 3. And if η3A is the appropriate η3 for inclusion in Figure 2, the error on y5 would arise from error-5, error-C, and error-B in Figure 3. Specifying the portion of the variance of y5 that arises from "error disruption" selects whether η3A or η3B or η3C is the variable the researcher views as contributing the complementary true-score portion of y5's variance.
The variance of indicator y5 is partitioned by the Figure 3 causal world, and Equations 2, 4, and 6 illustrate how any one of the latent variables η3C, η3B, or η3A could be validly introduced as η3 in Figure 2 by fixing y5’s error variance at the sum of the appropriate error variances presented within braces above.
A second indicator and potential incompatibility
To determine whether η3A, η3B, or η3C is validly used in the Figure 2 model, the researcher must consider more than just the identity and causal termini of disruptive “error” variables. They must also consider any additional available indicators such as y6. Figure 3 depicts η3A as an indirect cause of y6, η3B as a direct cause of y6, and η3C as not causing y6. Consider what would go wrong "statistically" (actually model implicationally) if η3 in Figure 2 was called, or given a “meaning,” corresponding to either η3A or η3C when in fact η3B was the direct causal source of y6. That is, consider the model implications, or model claims, that go awry if η3 (in Figure 2) were mis-identified as η3A or η3C because y6 was directly caused by η3B (as in Figure 3).
The covariance on the left of these equations is what the Figure 2 model, with its common-cause structure and effect magnitudes, implies should be observed as the covariance between y5 and y6 for the three optional meanings for η3. Naturally, since we are seeking a valid model, we hope the model’s implication matches the observed data covariance between y5 and y6.
Now return to Figure 3 and notice that the variances of variables η3A, η3B and η3C differ; with η3A having the smallest variance and η3C the largest variance because the variance-producing causal actions of additional “error” variables impinge on the chain of latent variables in moving from η3A toward η3C. Any of these different latent variances, when placed on the right sides of Equations 8, 9, or 10, could imply a covariance (on the left of the equation) that matches the observed y5 y6 covariance by making a compensating adjustment to the “estimated” magnitude of the effect leading from each latent-option to y6. The latent with the largest variance (η3C), could be given the weakest estimated effect leading to y6 to make the product of the entries on the right of Equation 8 correspond to the observed Cov(y5,y6), and so forth.
Hence, altering whether we choose η3A, η3B, or η3C to be the η3 to use in the Figure 2 model would control the magnitude of the “estimated” effect leading to y6 that would match the data covariance between y5 and y6. But only one of the causal connections would be valid in the sense of matching the world's causal structure (η3B if Figure 3 depicts the true causal structure) even though the other optional latents (η3A and η3C) could be made to match the covariance between the y5 and y6 indicators via compensating (but incorrect or “biased”) estimates of the effect leading from the selected latent to y6.
No estimate bias would arise if Figure 2 presented y6’s proper causal source, and we specified y5’s error variance as the sum of the error-5 and error-C (from Figure 3) because that selects η3B and implies use of Equation 9, which in turn results in an appropriate estimate for η3B’s effect on y6. But selecting either η3A or η3C to appear in Figure 2 (via accumulation of more or fewer errors in Figure 3) would result in an incorrect (biased) estimate of the effect of η3 on y6. η3A has too little variance to match the data Cov(y5,y6) with the proper size of effect, and η3C has too much variance to match Cov(y5,y6) with a proper size of effect. In fact, if Figure 3 constitutes the proper causal structure, η3C has no causal effect on y6, and any estimate other than zero is a biased estimate.
Latent theory and potential incompatibility
The effect leading from η3 to y6 contributes to producing and accounting for many additional data covariances. A zero η3 to y6 effect would causally disconnected y6 from all the other model indicators in Figure 2, and hence y6 would display zero covariance with all those indicators. A stronger η3 to y6 effect would imply stronger y6 covariances with the indicators of all the causes and effects of η3, not just with y5.
The latent-level effects leading to and from η3 in the Figure 2 model also depend upon η3 having a specific identity – whether η3A, η3B, or η3C. According to Figure 3, η3B is the appropriate version of η3 for matching the covariance between y5 and y6, but we have not yet confirmed that η3B is also the version of η3 required to engage in causal actions at the latent level of the Figure 2 model – where η3 receives effects from η1 and η2, and sends effects to η4 and beyond. In Figure 2, η3A might be required as the causal mechanism carrying effects from η1 and η2 toward the causally down-stream latents (and their indicators), and η3A might also be the version of η3 required to act as a common cause coordinating causally down-stream latents (and their indicators). Thus the latent level causal actions might call for η3A (in Figure 2) with its lower variance and (biasedly) stronger effect to y6 (via Equation 10), while the covariance between y5 and y6 calls for latent η3B with its higher variance and weaker effect leading to y6 (via Equation 9). Such inconsistencies constitute model misspecification and result in invalid models, biased estimates, and model ill fit. Hence both the latent-to-latent effects (as in Figure 2) and the single/multiple indicator options (as in Figure 3) must be assessed simultaneously in deciding which meaning of a latent (like η3) is appropriate for inclusion in the model. Similarly detailed assessments should accompany each fixed measurement error variance in the model (e.g. for y1, y3, etc. in Figure 2).
Figures 4B and 4C are similarly structured to display optional latent-variable identities corresponding to specific indicators, where dashed arrows indicate the kinds of latent-to-latent causal actions a researcher should consider in differentiating between the latent-identities η3A, η3B, and η3C. The selected latent identity might reflect a common disciplinary perspective (e.g, η3C in Figure 4B) but the selection should express the researcher’s theoretical preference and the availability of indicators of the other postulated latent causes/effects, rather than consensus. For example, if the Figure 4C data set had no indicator of “minimum duration for prayer” (or other variables influencing η3C), and if the researcher believed no effects led from η3C to downstream latent variables, the researcher would be pushed toward using η3B – namely toward a latent-identity assigning the variance in y5 produced by “minimum duration” (or other η3C causes) as error variance, not true latent variance. That is, attaining a valid model specification might require specifying y5 as containing a greater proportion of “error”.
Now back to Figure 3. If η3A is required to appropriately model the covariances of both y5 and y6 with the indicators of the other modeled latents, while η3B is required to model the covariance between y5 and y6, the estimation process will attempt to locate compromise estimates for η3’s effect on y6, and the effects connecting η3 to the other latents. Those compromise estimates can nonetheless result in noticeable inconsistencies between the covariance data and the model’s covariance implications. Such potential inconsistencies render the model testable, but before we turn to testing, let us reconsider the latent level of the model.
A new beginning: single indicators as encouraging precision in latent theory
Presuming Figure 3 depicts the true causal structure connecting y5 and y6, we could include both η3B and η3C as latents with single indicators in the model. We do not have to choose just one of η3A, η3B, or η3C. We could use y5 as an indicator of η3C, and y6 as an indicator of η3B, and add precision to the latent level of the model by assessing whether the latent-level effects connected to η3 in Figure 2 enter into, or emerge from, specifically η3B, or η3C, or both. For example, the effect from η1 might enter at η3B while the effect from η2 enters at η3C, and effects might emerge from either η3B or η3C or both on their way to causally-downstream latent variables. Careful consideration of the relevant latent-to-latent effects would be required, and error-C and error-B constitute important parts of the consideration. The variables comprising error-C will have no impact on any latents (other than η3C) unless η3C causes some other latent(s) in the model. In contrast, the real variables constituting error-B would influence whatever other latents were caused by either η3B or η3C.
If Figure 3 provides the proper causal specification for y5 and y6, using both y5 and y6 as single indicators would not permit incorporating both η3A and η3B in the latent level of the model. Either y5 or y6 alone could be used as a valid single indicator of η3A because η3A causes both, and the “intervening” error variables are presumed to be statistically independent, so there is an appropriate style of error accumulation that could be used. But the "other" indicator (whether y6 or y5) could not be used simultaneously as a direct indicator of η3B without misspecifying the causal actions of the variables constituting error-B. For y5 to be an indicator of η3A, the real causal actions constituting error-B would have to be part of what is cumulated into y5's error. For y6 to simultaneously be an indicator of η3B, those same real error-B sources would have to contribute true variance in η3B – which is contradictory because these real error-B sources cannot be both sequestered as measurement errors dead-ending in y5 and simultaneously be variables causing true-score variance in latent η3B and any variables causally down-stream from η3B.
y5 by itself would permit incorporating any one of η3A, η3B, or η3C in the latent level of the model (with error independence and the appropriate accumulation of errors as discussed above), and y6 by itself would permit inclusion of η3A or η3B in the model (with appropriate error accumulation). Using y5 and y6 as two single-indicators would permit use of both η3B and η3C in the model but not η3A and η3B. Using both y5 and y6 as multiple indicators of a single latent would permit only η3B in the latent level model (not η3A or η3C). y6 could never be justifiably used as an indicator of η3C in any model (even though y6 correlates with η3C due to common cause η3B) because the variables constituting error-C do not cause y6. With the causal structuring in Figure 3, using y5 and y6 as multiple indicators of a latent would demand use of η3B at the latent level in Figure 2, whereas use of a single indicator, or a pair of single indicators, would permit the latent level of the model to contain η3A alone, or η3B alone, or η3C alone, or both η3B and η3C.
Just as η3B is demanded by modeling y5 and y6 as two indicators of a single latent, multiple indicators in factor analysis demand indicator-controlled latent identities with minimal attention to whether or not the selected latent is capable of appropriate latent-to-latent causal actions. Factor analysis, and scales created from factor-based analyses, force a data-controlled identity onto latents like η3B while disregarding, or even disrespecting, theoretical concern for whether η3A, η3B, or η3C is, or are, required for appropriate latent level effects. The specification of η3 (in Figure 2) as η3A, η3B, or η3C should not be thought of as being under the exclusive control of η3's indicators. η3's identity is also tied to its latent effects (and absences of effects). The researcher should acknowledge the potential conflict between the latent-level and indicator-level identifications/meanings for η3 and preemptively attend to this by holistically assessing both η3's latent level effects and the indicators’ methodology (instrumentation, wordings, scaling, etc.). These observations illustrate why it is preferable to estimate a single full structural equation model rather than attempting to do measurement prior to incorporating latent level effects (as discussed in the 7(1) issue of Structural Equation Modeling). The detailed latent considerations prompted by consideration of single indicators should enhance the precision and research contribution provided by structural equation models.
A fixed 1.0 “loading” and a fixed measurement error variance are sufficient to statistically-identify the latent but the larger the fixed measurement error variance the less precise the meaningful-identity provided by a lone indicator. As the specified measurement error variance increases, the latent’s identity is loosened because the latent could be any latent capable of accounting for a decreased proportion of the indicator’s variance. Consequently, latent-level model constraints take stronger control of the latent’s identify with larger measurement error variance specifications. The saturated latent covariances for η3 in Figure 1 hamper specification of a consistent latent-and-indicator based identity for η3 because the absence of specific required and forbidden latent-level causal connections impedes meaningful differentiation between η3A, η3B and η3C. A factor analytic claim that η3 displays unspecified correlations with other latent factors is too imprecise (too unconstraining) to contribute substantively to identifying η3.
As the researcher attends to η3's required (hopefully few) and forbidden (usefully many) latent causes and effects, η3's identity solidifies in the researcher's understanding. That clarified understanding contributes importantly to assessing the strengths and weaknesses of whatever indicators are vying for designation as the “best indicator” because this focuses attention on the specific variables constituting the errors like error-5, error-C, and error-B. Some causes of the optional latent identities might be slated to appear in the model (like η1 and η2 in Figure 2), and that contributes importantly to deciding whether the required latent is η3A, η3B, or η3C. Assessing which variables’ causal impacts do, or do not, enter between the η3 true scores and the indicators’ values clarifies what constitutes measurement error. Researchers may end up disagreeing over the latent’s preferred identity but this constitutes research advancement because it clarifies disagreements previously obscured by conceptual imprecision.
Once the meaning or identity of each latent corresponds to the researcher’s current theoretical understandings, the researcher faces the challenge of getting the model to comply with those understandings so that when data speak about the model they also speak directly about the researcher’s understandings. Most researchers are comfortable incorporating theory assertions about latent effects and absences of effects (as in Figure 2) but researchers should be equally comfortable making measurement error variance assertions because measurement assertions are a type of theory assertion.
An effective procedure for maintaining intended theoretical latent meanings was developed decades ago (e.g. Entwisle, Hayduk & Reilly ), and was illustrated in Hayduk , and summarized in Hayduk . Hayduk’s procedure, as it was dubbed on SEMNET, requires specifying a fixed non-zero measurement error variance for each indicator receiving a 1.0 effect/loading. Fixed measurement error variances are thus provided for all single-indicators, and for the best indicator within each set of multiple indicators. (The other indicators in multiple indicator sets are typically given free loadings and measurement error variances.) The fixed 1.0 provides a scale for the latent and the fixed measurement error variance selects from alternative latent meanings, as in Figures 3 and 4. But before we consider the practical details of fixing measurement error variances, we should consider the statistical identification of the model, and model testing. The fixed measurement error variance procedure we recommend constitutes neither the minimum requirement for model identification nor excessive measurement assertiveness.
Identification, testing, and what is tested
If, as in Figure 1, there were four latents and hence eight indicators in the model, there would be 8(8+1)/2 = 36 indicator variances and covariances as data points. The estimated model coefficients would include: 4(4+1)/2 or 10 variances and covariances of the latents, four "loadings" (the other four being fixed 1.0’s scaling the latents), and eight measurement error variances – for a total of 22 estimates. Barring empirical underidentification (which presumes there are no entirely redundant indicators, no entirely disconnected latents or indicators, or indicators having zero variance) these 22 model coefficients should be estimable, and the Figure 1 model should provide a mode χ2 test having 36 - 22 = 14 degrees of freedom.
The Figure 2 model would be more assuredly identified than the Figure 1 model, again barring empirical underidentification, which now also presumes no new identification concerns for reciprocal latent effects, loops, excessive latent error covariances, and the like. If there are two fewer effects between the latents than there are covariances among the Figure 1 latents, the Figure 2 model has two more degrees of freedom than the Figure 1 model. And if a fixed measurement error variance is specified for the best of each pair of indicators, this contributes four additional degrees of freedom, making a total of 20 degrees of freedom for the Figure 2 model χ2 test. Fixed measurement error variances may be needed to statistically identify some models, but that is not why we need them in the current context, or recommend them in general. The fundamental justification is that fixed measurement error variances clarify the modeled theory, and hence improve the investigation and testing of theory.
Unfortunately, there is no thorough, accurate, and easy specification of what either the Figure 1 or Figure 2 model tests test. It is not as simple as saying Figure 1 tests whether there is a latent underlying each pair of indicators, while a χ2–difference test (created as the difference in χ2 values and difference in degrees of freedom between the Figure 1 and Figure 2 models) tests whether the postulated latent effects and asserted measurement error variances are correct. These claims are stifled by the possibility that the absence of latent level and measurement error variance constraints permit the Figure 1 model to contain inappropriate compromise latents. Remember that with y5 and y6 as multiple indicators it is impossible to have either η3A or η3C as the η3 latent in Figure 1. The absence of specified latent causal constraints on η3 in Figure 1 makes it comparatively easy for the Figure 1 model to estimate η3 as being η3B (to match the y5- y6 covariance) even if latent η3A was required to match η3’s latent-level causal actions. The more stringent latent-level causal requirements on η3 in the Figure 2 model make it more difficult for the estimation process to match the data covariances with an inconsistent η3 identity. A model requiring η3A will tend to fail even if the appropriate latent-level causal connections for η3A are specified in the Figure 2 model because the covariance between y5 and y6 requires η3B. The presence of both y5 and y6 as multiple-indicators pushes for use of η3B in both the Figure 1 and Figure 2 models, but the inconsistency of this forced use of η3B (when η3A is required) is less detectable in Figure 1. The more specific and more demanding latent causal constraints on η3 in Figure 2 make it easier to detect the inconsistency between one part of the model (the latent level) requiring η3A with its smaller variance, while another part of the model (the latent common cause of y5 and y6) requires η3B with its larger variance. The Figure 1 model has sufficient degrees of freedom to detect many mis-identifications of latents, but the Figure 2 model has even more degrees of freedom, and its restrictive latent causal claims assist detection of additional inconsistencies.
We caution against thinking the nesting of the Figure 2 model within the Figure 1 model permits confident use of a χ2-difference test as testing just the constraints added (the coefficients given fixed values) in moving to the Figure 2 model. An ill-fitting Figure 1 model clearly reports evidence of problems beyond or without the added constraints – so a fitting Figure 1 model is a precondition for any such claim. If the less-restricted Figure 1 model is properly causally specified (despite containing some unnecessarily free latent covariances), then the χ2-difference test does indeed test the added constraints, but notice that the fit of the Figure 1 model does not assure us that the Figure 1 model actually is causally proper. The model may have managed to fit by choosing an incorrect compromise identity for a variable like η3, or incorrect identities for several latent variables. Hence the failure of the more restricted (Figure 2) model may, or may not, be signaling the improperness of even a fitting Figure 1 style model. The failure of a Figure 2 model might result from incorrect placement of null causal connections between some latent effects (so rearrangement of the latent effects could render the model proper) but the failure of the more restricted model might instead be reporting that some latent variables in the Figure 1 model were problematic, even if initially undetectably so.
Adding indicators clustered under specific latents, while retaining a saturated latent-level model like Figure 1, provides additional testing but it is testing that fails to cogently test whether the latents can be appropriately coordinated by latent-to-latent causal actions. A fitting Figure 1 style model with additional clustered indicators, provides evidence that only one latent underlies the clustered items, but this can be a Trojan horse surreptitiously sneaking in a latent like η3B rather than a proper causally-connectable η3A or η3C. More indicators (even in fitting Figure 1 style models) do not necessarily mean better latents, they mean more entrenched latents – where the entrenchment is provided by the indicators, with the possible sacrifice of appropriate latent-level causal connectivity.
Researchers locating latents via factor analysis have statistically/procedurally avoided stringent examination of whether the located latent factors are capable of engaging in causal actions at the latent level – and hence these researchers are prone to being rudely surprised when their “meaningful” latent factors fail to behave appropriately as latent causes and effects. Cross-over loadings leading from one latent to indicators of another latent exacerbate the problem of factor models morphing (via biased estimates) into χ2-fitting but causally-problematic models (see Hayduk & Glaser ). And using scales created by adding or averaging the values of multiple indicators make it more difficult to distinguish between latents such as η3A, η3B, and η3C because only the scale’s covariances appear in the data covariance matrix rather than the multiple indicators’ covariances. That makes the model less able to detect the type of inconsistency discussed above.
Collectively, these observations preclude making simple statements about what structural equation model tests test, even without enumerating the many additional features potentially leading to significant model ill fit – features such as violation of the presumed causal homogeneity of the cases, non-normality, or non-linearity. What remains undeniable is that any model with a fixed measurement error variance for either a single indicator, or best of multiple indicators, is more assuredly identified than the same model with a free (and potentially identification-disrupting) measurement error variance.
Specifying measurement error variances for single indicators and the best of multiple indicators
How then is a researcher to proceed? Our advice is to begin with a model that seems reasonable to you as researcher, and that is theoretically precise – a model like Figure 2 with constraints on the latent-level effects and constraints on the latent-to-indicator effects (whether this means using y5 as a single indicator of η3A, or y5 and y6 as multiple indicators of η3B, or y5 and y6 as single-indicators of both η3C and η3B). This model should contain a fixed (usually nonzero) measurement error variance for each indicator having a 1.0 loading that specifies a scale for a latent – namely for the best (possibly the only) available indicator of each latent.
To obtain a fixed numerical measurement error variance, the researcher begins by carefully considering the latent level causal structure, to gain a clear sense of how each latent is expected to causally function with respect to the other modeled latents and with respect to specific imagined error variables like error-A, error-B, error-C and error-5 in Figure 3. The researcher explicitly considers how far the causal consequences of each specific imagined error would spread through the model. The researcher then seeks the best, or few best, indicators for each latent. “Best” here refers to the indicator most clearly reflecting the researcher’s desired meaning for each latent. For indicators obtained from questionnaires, the researcher should consider whether the respondents know themselves in ways that permit even truthful and uninhibited responses to causally originate in the values of the intended latent. The question wording, the context provided by other questions, and the available response options are all relevant to this assessment. The researcher should filter out questions having confusing or inappropriate wordings, likely misinterpretations, insufficient or unclear response options, and restricted or skewed response ranges.
There is no good reason to shade one’s measurement error variance assessment to be artificially small. Such a preference constitutes a bias against a latent like η3A because using y5 as an indicator of η3A requires cumulating more errors. But notice that the measurement error variance specification for y5 might justifiably use a smaller error variance specification than suggested by y5’s loading or reliability from prior factor analyses. Other researchers may have used y5 to locate η3B via factor analysis (with additional indicators like y6) but that does not forbid the current researcher from using η3C as their latent, which would require a smaller error variance on y5 than was observed in factor analysis. Measurement error is not something vaguely "out there", and it is not something reported exclusively by an item’s methodology. What is modeled as measurement error also depends crucially on the researcher’s theory assertions and theory postulations. What counts as measurement error is intimately tied to the current researcher’s theory requirements and intentions. (Does η3A, η3B, or η3C belong in the theory?) Error variance specifications attend to theory consistency, not merely to indicator correlations.
For example, if η3A, η3B, and η3C in Figure 3 each directly caused the severity of one medical symptom, the resultant correlated-symptoms would not warrant claiming there was only a single underlying latent cause. Diagnostic symptom-sets address a variety of clinical exigencies but may or may not be properly specified as multiple indicators having one common cause. Structural equation researchers must learn to beware administratively routine variables whose causal foundations are imprecise or even misconceived. Similarly, beware the term “breadth”. All latent variables, including factors, have no “breadth” (they only have a magnitude or value on a skinny number line) no matter how many indicators or effects they have. Adding indicators does not add breadth to the latent – it adds additional concern for the properness of the model’s causal specification. The quality of coefficient estimation will decline if indicators are causally misspecified as multiple indicators.
Both the measurement error variance assessments and the model’s latent structure should reflect any methodological concerns with the indicators, including methodological mess-ups. If a methodological mess-up causally influenced the data, appropriately including that mess-up as part of the latent-level causal model adds explained, not error, variance and would result in unbiased estimates of the other model coefficients [16:31, xix]. Consider how a researcher might address the causal consequences of having several indicators obtained by the same method. We hesitate to say the concern is for a “specific factor” or “method factor” because some people would presume the only reasonable way to address this would be by adopting a traditional factor approach. A superior procedure might be to obtain the best indicator for a method-latent by selecting an indicator using the method but whose substance was disconnected from the other modeled latents. That best method-indicator should scale the method-latent with a fixed 1.0 loading and be given a fixed measurement error variance (the variance arising from everything except the method’s variance). The effects of the method-latent on all the other relevant indicators should be constrained to be equal unless theory justifies why some indicators should display more method’s response than others. This results in only two coefficients to estimate – the variance of the method latent and the effect magnitude connecting the method-latent to all the relevant indicators – and adds model degrees of freedom due to the new indicator’s numerous new data covariances. Selecting the “best indicator” of the method latent, specifying a fixed measurement error variance for that best indicator, and considering possible causal connections between the method latent and the other modeled latents would do more to clarify the nature of the measurement-method’s causal nexus than would a knee-jerk reaction pretending that calling something a “methods factor” requires use of an ordinary “factor”.
Indeed, it may sometimes be possible to model two latents (one being the latent of interest, the other being a specific or “method-factor” latent) with only a single indicator if the two latents are clearly and substantially differentially embedded at the latent level of the model. Unfortunately, the required and forbidden latent level causal relationships of “methods-factors” seem insufficiently specified in existing theories, though we hope awareness of this modeling possibility encourages appropriate theory developments. Other methodological concerns might involve violation of the presumed independence of the latent-level errors in Figure 3, or an unmeasured cause of an intended latent also causing an indicator via mechanisms not currently in the model. These kinds of concerns can be addressed but require modeling tricks beyond what we can discuss here (see Chapter 7 of , or ).
Obtaining the specific numerical value to use as a fixed measurement error variance is often assisted by the researcher making their assessments as percents of the indicator’s variance that are likely to originate in the various potential causal sources of the indicator (the things paralleling error-5, or error-C, etc. in Figure 3). The researcher then obtains their specific asserted numerical value for the indicator’s fixed measurement error variance by multiplying the actual variance of the indicator by the sum of the percents assigned the features the researcher claims as error sources (all the things comprising error-5, or perhaps the things comprising both error-5 and error-C, and so on). Notice that the indicator's measurement error variance specification does not depend on how well the researcher expects the corresponding latent to be explained, or how well it explains other latents. An indicator that contains much measurement error, can correspond to a latent that explains much or little, or that is explained well or poorly by other latents – depending on the model and the operative real-world forces.
Those unaccustomed to making error variance assessments might familiarize themselves with the sensitivity of variance to the placement of extreme cases in a variable’s distribution by duplicating a variable from a data set (so the real data remains pristine) and using their favorite program to plot the variable’s distribution and calculate the variable’s variance when some cases’ values are changed, for example by: moving some values from below the mean to above the mean, taking central values and making them extreme, taking extreme values and making them central, moving many or all the cases’ values up, or randomly moving some cases’ values up and others down. Observing the distributional changes, and percentage changes in variance, that result from such artificial causal interventions assist in making more realistic error variance assessments. For example, if a variable has a skinny-tailed distribution, only a very few cases are likely to have obtained extreme values “in error” because only a portion of the already-few extreme cases are likely to have obtained those values erroneously. Assessments of error variances must respect the observed variable’s distribution.
Some researchers experience an urge to estimate as many measurement error variances as possible – thereby avoiding fixed measurement error variances. We recommend researchers curb this urge for the sake of theory precision. Being able to estimate a measurement error variance does not mean one should do this. Specifying a fixed measurement error variance for the best available indicator assists model identification (or over-identification), but this is not done because the researcher must do this for model identification. The fixed measurement error variance contributes to theoretical precision. Freeing the measurement error variance on the best available indicator amounts to succumbing to an estimation-invitation to theoretical imprecision. (The measurement error variance on a second indicator is typically left free because once the latent’s identity has been controlled by the best indicator’s specification, the second indicator’s free loading and measurement error variance provide an assessment of how good or poor that second-best indicator is at reflecting the latent specified via the best-indicator.) Even single indicators can have identified measurement error variances (for example, if the single-indicated latent also causes several other latents) but here also the researcher should demonstrate their commitment to theory by resisting estimation of the single-indicator’s measurement error variance.
Others feel an urge to estimate as many error variances as possible, to avoid those specifications potentially contributing to model failure. This inclines the researcher toward theory-imprecision merely to reduce the possibility that the data will speak against their theory. Making a theory imprecise does indeed make it more difficult for the data to detect problems in the theory – but that same imprecision makes it easier for the discipline to disregard the researcher’s work! Researchers using “lack of certainty” as an excuse to estimate the best indicator’s measurement error variance should be heard as theory bashing, theory belittling, or theory deficient – depending on whether their statement is made brutishly, snidely, or as an honest expression of incapacity as theorist. From the factor-analytic perspective, a fixed measurement error variance is non-conventional, though the extra theory-precision clearly supersedes factor-analytic tradition.
What if the theory-laden model fails to fit?
If a Figure 2 style model fails to fit the data according to χ2, this provides evidence that something has gone wrong. Unfortunately there is no generally-applicable procedure that can assuredly identify specifically which of the many potentially problematic things has gone awry. The best the researcher can do is report and respect the evidence of problems, and seek diagnostic signs pointing toward or away from specific possible problems.
The modification indices might suggest improving the fit by freeing the fixed measurement error variance on y5 (putatively the best available indicator), but this should not be done without a thorough reconsideration of the features discussed above. The corresponding "expected parameter change" statistic might suggest increasing or decreasing y5's fixed measurement error variance, where increases or decreases should be thought of as moving up or down among latents like η3A, η3B, and η3C. But remember that latents like η3A might never be modelable if both y5 and y6 are used as multiple indicators in the model. Instead of freeing y5's measurement error variance at the behest of the modification index, the researcher might decide to drop y6 and thereby permit changing the fixed error variance on y5 to locate η3A. Or the researcher might decide to make y5 an indicator of η3C and y6 an indicator of η3B so that both y5 and y6 receive fixed measurement error variances, and the model contains two similar yet distinct η3 latents (η3B and η3C). With y5 and y6 as single indicators of separate latents, the complex but theory-beneficial reconsiderations would focus on how theory could incorporate two slightly different versions of what previously had been incorrectly thought of as a single latent η3.
Or suppose a substantial modification index appeared for the covariance between the errors on y5 and y6. This might signal need for coordination between these errors, but error covariances are frequently inserted without sufficient consideration. Measurement error variables are routinely assumed to be independent of the latents in the model, and that renders the causal foundations of measurement error covariances entirely disconnected from the original latent theory. Consequently, freed measurement error covariances tend to become fudge-factors that provide fit without any theory justification. It is preferable to view a substantial modification index for an error covariance on indicators like y5 and y6 as indicating the constraints in some portion of the model are incompatible with the constraints specifying y5 and y6 as originating in the common cause η3B. Thus the researcher’s thought process returns to considering Figures 3 and 4 and the various ways of responding to possibilities like η3A and η3C. This keeps any subsequent model modifications intimately connected to the researcher’s original theory. The researcher should report whatever model modifications are made at the behest of the modification indices because these are theory-focused model revisions.
Notice that modification indices are unable to directly call for inclusion of new latent variables, or for removal of improper even if biasedly-significant effects. Also notice that if the researcher had used a scale (created from y5 and y6) as the indicator for η3 that would further impair the ability of the modification indices and other diagnostics to prod consideration of y5 and y6 as indicators of separate latents. A substantial modification index connected to a scale should initiate substantive reconsideration of all the items comprising that scale.
In short, the diagnostic investigation should be oriented toward theory reconsideration and theory revision, with fit or fail as secondary to the theory legacy. The researcher should report any incorporated changes as theory modifications – and maybe even theory advances – but this is getting uncomfortably close to indirect data snooping that biases model testing. Fortunately, entertaining the possibility of new and differentially causally embedded latents is not as statistically odious as directly following large modification indices. The retheorizing provides a research contribution whether or not it results in a fitting model.
The only way a fixed measurement error variance on a single-indicator contributes to model ill fit, or has a substantial modification index, is if that measurement error variance would be "identified if freed". The modification index and expected parameter change statistics could clearly point to this style of problematic coefficient. In contrast, a fixed measurement error variance that would be underidentified (un-estimable) if freed does not contribute to model ill fit and will have a zero modification index even if the current fixed measurement error variance value is too small or too large. For example, if y5 was a single indicator and its error variance was not rendered identified by the latent level of the model, the fit and modification indices would be unable to signal a problematic error variance specification, or warn of the biases in the latent effect estimates that might arise from this. The amount of bias introduced by undetectable measurement error misspecification depends on many things, the most important being the magnitude of the misspecification. For example, if y5’s underidentified-if-freed measurement error variance was fixed at zero (thereby claiming no measurement error), the extent of the bias this introduces would depend on whether the true latent was η3A, η3B , or η3C. If the true latent was η3A, the fixed zero value would be most-misspecified and the coefficient estimates most biased – even if undetectably biased.
This style of problem commonly appears when demographic variables like sex or age are assigned zero measurement error variance. There is clearly some measurement error variance in age – because age accumulates progressively even if measured in years. Measurement error in reported sex becomes more obvious if one considers some respondents as “reporting a wrong sex just for the fun of it,” or models where the latent effects of sex arise from the number of Y chromosomes rather than self-labeling or from genital appearance (which may have been “surgically assigned” just after birth, or reassigned later in life). The estimated effects of age and sex will be biased unless the appropriate measurement error is entered into the model – whether or not the omitted measurement error variance on age or sex results in noticeable ill fit or modification indices. Specifying a small non-zero measurement error variance for any single indicator (for age, sex, or whatever) is likely to provide less-biased estimates than an obviously-wrong specification of zero measurement error variance, but to consider this carefully one must again consider the causal forces preventing the indicator from precisely tracking the values of the intended latent variable. We empathize with those struggling to determine the amount of measurement error to specify, but we will rebuke anyone who pretends the difficulty justifies specifying zero measurement error variance – because that pretends the difficulty of the task justifies using an extreme and unjustified value (zero).
Fortunately, there is a relatively simple way to assess the consequences of specific fixed measurement error variances on single indicators whether or not they would be underidentified if freed. The strategy has been dubbed the “half and double” procedure, and was popularized by Hayduk (, page 125; , page 28). The consequences of an incorrect measurement error variance assessment can be assessed by running a series of models, each altering one fixed error variance to first "half” and then “double" the original fixed value. Half the researcher’s best assessment of the measurement error variance makes the measurement error variance about as low as it might reasonably be (it is half way to the unreasonable value of zero), and double makes this about as high as it might reasonably be. For each run the researcher monitors the other coefficient estimates (especially those directly connected to the latent whose measurement quality is being tickled) to see how sensitive those estimates are to the alternative measurement error variance specifications. Any substantial variation in estimates warrants careful consideration and report because these particular coefficient estimates are especially sensitive to the researcher’s corresponding measurement error variance specification.
The background for the Figure 5 model is that back in 1985 a common factor model for the repeat personal space measurements failed convincingly. The measurements all used the same methodology, with the same participants, in the same baseline/control context, but the repeated measurements did NOT measure the same thing! A simplex model (a straight line of causal effects) fit via χ2, but that ordinary simplex model did not correspond to a comfortable or causally-understandable theory for these data. Nearly a decade passed before the fitting, understandable, and theory-helpful, loop-simplex model in Figure 5 was developed (Hayduk ). The 1.0 values connecting the latents in this model indicate that each subject’s spatial preference would have persisted perfectly from one measurement occasion to the next were it not for the structural disturbance terms and causal feedbacks modeled as self-causative loops at each successive measurement. This model illustrates a nearly-identical set of single indicators supporting a theoretically complex and somewhat unusual model structure – a model structure matching how the subjects’ brains acted causally in determining the subjects’ momentary spatial preferences. Additional single-indicator models permitted even closer parallels to causal neurological activity but this is not the place to discuss how the brain functions, or to explicate the statistical details of how causal-loops function, so we must be satisfied with referring the reader to Hayduk (,  Chapter 3) for further discussion of the theory in the Figure 5 model.
Summary and discussion
The gist of the above is that each single indicator of a latent, and the best indicator from each set of multiple indicators, should be provided a fixed 1.0 “loading” and a fixed measurement error variance based on the researcher’s assessment of both the indicator’s methodology and the focal latent’s causal connections to the other latents. The fixed 1.0 loading scales the latent and the fixed measurement error variance assigns a theory-dictated identity or meaning to the latent. This is not done on the basis of what the researcher unerringly knows, but on the basis of what the researcher thinks s/he knows, so that the data via the estimates, testing, and diagnostics, speak to what the researcher thinks s/he knows. Any additional indicators believed to originate in the latent are given free loadings and free measurement error variances. While this description and our discussion focuses on reflective indicators, it should be clear that similar observations apply to both formative and reactive  indicators. The fundamental concern is for valid and precise latent-indicator representations no matter what style of measurement structure is involved.
Understanding that the latent variable absorbing and emitting latent-level effects must match the latent variable influencing that latent’s indicators reveals why multiple indicators located by factor analysis tend to fail when incorporated in structural equation models. Free factor correlations place no latent level constraints on the factors, and hence latent factors are permitted to become variables that are unable to function causally appropriately with respect to other latents. Even fitting factor models provide no assurance that the latent common factor causes of the indicators will function causally-appropriately with respect to other latents. Consequently, introducing latent level theoretical constraints often challenge the causal appropriateness of factors connected to multiple indicators. Researchers should hear saturated factor correlations and entirely free measurement error variances as shouting THEORY IMPRECISION regarding the latent-level causal structure.
The existence of multiple similarly worded indicators is no longer a license to squelch theory by saturating the latent level of the model with factor correlations, or by failing to assert a latent’s meaning with a fixed measurement error variance for the best of the multiple indicators. Focusing on single indicators, and designating the best of multiple indicators, encourages attention to each latent and indicator, and constitutes a call to theorize carefully. The identity of latents is not resolved by appealing to just the data – this unavoidably involves the researcher’s understandings and causal theory . It is dubious to attempt “measurement” prior to “theory”, or factor analysis prior to full structural equation modeling, because there is no routine assurance that latents functioning as common causes of the indicators will assuredly function appropriately as causally-coordinateable latents.
If a full structural equation model fails and provides diagnostics questioning some second or weaker indicator, the researcher might drop that indicator but it would be preferable to retain the indicator by making it a single indicator of a similar yet theoretically distinct latent whose causal coordinations deserve explication. Much is also gained by using single indicators to incorporate multiple-regression-like control for potentially confounded variables. If the model requires control for sex, age, disease severity, number of friends, happiness, or belief in an after-life, the relevant control variables are latents because they likely contain measurement error. There seems little reason to require more than a single even if error-containing indicator for sex or age, but it is important to realize that the researcher could also statistically control for the other listed variables with single indicators. The researcher must decide whether a stronger research contribution would arise from using an additional indicator as a redundant multiple indicator of some currently-modeled latent, or by using that additional indicator to control for some causal mechanism currently omitted from the model. One does not need multiple indicators to locate a mechanism carrying a postulated effect, to extend a theory’s reach, or defend a theory’s claims by controlling some confounder. Hence the choice will often favor a single indicator controlling for some theory-relevant feature rather than multiply entrenching a particular latent.
Single indicators forcefully remind us that measurement is not separate from theory. Theoryphobes may consider single indicators too theory demanding, but researchers should think of single indicators as theory-encouraging and theory-invigorating. Single indicators challenge people to join the community of researchers, where one's constant environ is imperfect-knowing, and where detailed attention to theory and methodology are one's most trustworthy guides. Careful consideration of single indicators encourages a close coordination between the researcher’s thinking and their structural model, whether any specific latent ends up with one, two, more, or even no , direct indicators. When researchers place their understandings in their models, they hear their data speaking to them because it is their understandings that are being revised if the data urges model modification. Conscientious use of single, or the few best, indicators contributes to theory/model precision but it remains for the world to dictate whether the precise theory/model is valid or precisely wrong.
We thank Greta Cummings and Susan Slaughter for helpful comments on early drafts of this article.
- Thurstone LL: Multiple Factor Analysis. 1947, Chicago: University of Chicago PressGoogle Scholar
- Harman HH: Modern Factor Analysis. 1967, Chicago: University of Chicago Press, 2Google Scholar
- Lawley DN, Maxwell AE: Factor Analysis as a Statistical Method. 1971, London: Butterworth & Co, 2Google Scholar
- Mulaik SA: The Foundations of Factor Analysis. 1972, New York: McGraw-HillGoogle Scholar
- Wright S: Correlation and causation. J Agric Res. 1921, 20: 557-585.Google Scholar
- Wright S: The method of path coefficients. Ann Math Stat. 1934, 5: 161-215. 10.1214/aoms/1177732676.View ArticleGoogle Scholar
- Blalock HM: Causal Inferences in Nonexperimental Research. 1964, Chapel Hill: University of North Carolina PressGoogle Scholar
- Duncan OD: Introduction to Structural Equation Models. 1975, New York: Academic PressGoogle Scholar
- Heise DR: Causal Analysis. 1975, New York: John Wiley and SonsGoogle Scholar
- Byrne BM: A Primer of LISREL: Basic Applications and Programming for Confirmatory Factor Analytic Models. 1989, New York: Springer-VerlagView ArticleGoogle Scholar
- Kline RB: Principles and Practice of Structural Equation Modeling. 2005, New York: Guilford PressGoogle Scholar
- Byrne BM: Structural Equation Modeling with LISREL, PRELIS, and SIMPLIS. 1998, Lawrence Erlbaum Associate: Mahwah NJGoogle Scholar
- Byrne BM: Structural Equation Modeling with EQS: Basic Concepts, Applications, and Programming. 2006, Lawrence Erlbaum Associates: Mahwah NJ, 2Google Scholar
- Bollen KA: Structural Equations with Latent Variables. 1989, New York: WileyView ArticleGoogle Scholar
- Hayduk LA: Structural Equation Modeling with LISREL: Essentials and Advances. 1987, Baltimore: Johns Hopkins University PressGoogle Scholar
- Hayduk LA: LISREL Issues, Debates and Strategies. 1996, Baltimore: Johns Hopkins University PressGoogle Scholar
- Anderson JC, Gerbing DW: Structural equation modeling in practice: a review and recommended two-step approach. Psychol Bull. 1988, 103: 411-423.View ArticleGoogle Scholar
- Anderson JC, Gerbing DW: Assumptions and comparative strengths of the two-step approach: comment on Fornell and Yi. Sociol Method Res. 1992, 20: 321-33. 10.1177/0049124192020003002.View ArticleGoogle Scholar
- Fornell C, Yi Y: Assumptions of the two-step approach to latent variable modeling. Sociol Method Res. 1992, 20: 291-320. 10.1177/0049124192020003001.View ArticleGoogle Scholar
- Fornell C, Yi Y: Assumptions of the two-step approach to latent modeling. Sociol Method Res. 1992, 20: 334-339. 10.1177/0049124192020003003.View ArticleGoogle Scholar
- SEMNET: The Structural Equation Modeling Discussion Network. http://www.aime.ua.edu/cgi-bin/wa?A0=SEMNET,
- Hayduk LA, Glaser DN: Jiving the four-step, waltzing around factor analysis, and other serious fun. Struct Equ Model. 2000, 7: 1-35. 10.1207/S15328007SEM0701_01.View ArticleGoogle Scholar
- Mulaik SA, Millsap RE: Doing the four-step right. Struct Equ Model. 2000, 7: 36-73. 10.1207/S15328007SEM0701_02.View ArticleGoogle Scholar
- Bollen KA: Modeling strategies: in search of the holy grail. Struct Equ Model. 2000, 7: 74-81. 10.1207/S15328007SEM0701_03.View ArticleGoogle Scholar
- Bentler PM: Rites, wrongs, and gold in model testing. Struct Equ Model. 2000, 7: 82-91. 10.1207/S15328007SEM0701_04.View ArticleGoogle Scholar
- Herting JR, Costner HL: Another perspective on the “proper number of factors” and the appropriate number of steps. Struct Equ Model. 2000, 7: 92-110. 10.1207/S15328007SEM0701_05.View ArticleGoogle Scholar
- Hayduk LA, Glaser DN: Doing the four-step, right-2-3, wrong-2-3: A brief reply to Mulaik and Millsap; Bollen; Bentler; and Herting and Costner. Struct Equ Model. 2000, 7: 111-123. 10.1207/S15328007SEM0701_06.View ArticleGoogle Scholar
- Barrett P: Structural equation modelling: Adjudging model fit. Personal Individ Differ. 2007, 42: 815-824. 10.1016/j.paid.2006.09.018.View ArticleGoogle Scholar
- Hayduk LA, Cummings GG, Boadu K, Pazderka-Robinson H, Boulianne S: Testing! Testing! One, two, three – Testing the theory in structural equation models!. Personal Individ Differ. 2007, 42: 841-850. 10.1016/j.paid.2006.10.001.View ArticleGoogle Scholar
- McIntosh CN: Rethinking fit assessment in structural equation modelling: A commentary and elaboration on Barrett (2007). Personal Individ Differ. 2007, 42: 859-867. 10.1016/j.paid.2006.09.020.View ArticleGoogle Scholar
- Millsap RE: Structural equation modeling made difficult. Personal Individ Differ. 2007, 42: 875-881. 10.1016/j.paid.2006.09.021.View ArticleGoogle Scholar
- Mulaik SA: There is a place for approximate fit in structural equation modelling. Personal Individ Differ. 2007, 42: 883-891. 10.1016/j.paid.2006.10.024.View ArticleGoogle Scholar
- Steiger JH: Understanding the limitations of global fit assessment in structural equation modeling. Personal Individ Differ. 2007, 42: 893-898. 10.1016/j.paid.2006.09.017.View ArticleGoogle Scholar
- Hayduk LA, Pazderka-Robinson H: Fighting to understand the world causally: Three battles connected to the causal implications of structural equation models. Pp 147-171 in Outhwaite W, Turner S (eds.), Sage Handbook of Social Science Methodology. 2007, London: Sage PublicationsGoogle Scholar
- Jöreskog K, Sörbom D: LISREL 8: Users Reference Guide. 1996, Chicago: Scientific Software InternationalGoogle Scholar
- Entwisle DR, Hayduk LA, Reilly TW: Early Schooling: Cognitive and Affective Outcomes. 1982, Baltimore: Johns Hopkins University PressGoogle Scholar
- Hayduk LA: Personal space: understanding the simplex model. J Nonverbal Behav. 1994, 18: 245-260. 10.1007/BF02170028.View ArticleGoogle Scholar
- Hayduk LA: Personal space: the conceptual and measurement implications of structural equation models. Can J Behav Sci. 1985, 17: 140-149.View ArticleGoogle Scholar
- Hayduk LA, Stratkotter RF, Rovers MW: Sexual orientation and the willingness of Catholic seminary students to conform to church teachings. J Sci Stud Relig. 1997, 36: 455-467. 10.2307/1387861.View ArticleGoogle Scholar
- Hayduk LA, Pazderka-Robinson H, Cummings GG, Boadu K, Verbeek EL, Perks TA: The weird world, and equally weird measurement models: Reactive indicators and the validity revolution. Struct Equ Model. 2007, 14: 280-310. 10.1080/10705510709336747.View ArticleGoogle Scholar
- Borsboom D, Mellenbergh GJ, van Heerden J: The concept of validity. Psychol Rev. 2004, 111: 1061-1071.View ArticlePubMedGoogle Scholar
- The pre-publication history for this paper can be accessed here:http://www.biomedcentral.com/1471-2288/12/159/prepub
This article is published under license to BioMed Central Ltd. This is an Open Access article distributed under the terms of the Creative Commons Attribution License (http://creativecommons.org/licenses/by/2.0), which permits unrestricted use, distribution, and reproduction in any medium, provided the original work is properly cited.