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Evaluating the quality of evidence from correlational research for evidence-based practice.

In their recent article in the Educational Researcher, Feuer, Towne, and Shavelson (2002) asked,

What are the most effective means of stimulating more and better scientific educational research? ... [T]he primary emphasis [italics added] should be on nurturing and reinforcing a scientific culture of educational research. (p. 4)

They defined scientific culture as "a set of norms and practices and an ethos of honesty, openness, and continuous reflection, including how research quality is judged" (Feuer, Towne, & Shavelson, 2002, p. 4, italics added). Recent movements to emphasize evidence-based practice in medicine (see Sackett, Straus, Richardson, Rosenberg, & Haynes, 2000), psychology (see Chambless, 1998), and education (Mosteller & Boruch, 2002; Shavelson & Towne, 2002) also reflect the necessity for standards with which to evaluate research evidence, including evidence from correlational designs.


Correlational studies can be defined in various ways. In one sense, all analyses are correlational (Cohen, 1968; Knapp, 1978; Thompson, 2000a). Because all conventional parametric analyses (e.g., t-tests, ANOVA, ANCOVA) are correlational (Bagozzi, Fornell, & Larcker, 1981), in a sense every quantitative study yields correlational evidence. Distinguishing evidence types by focusing on the analysis is not useful because under such a broad definition, all evidence would fall under this single umbrella. Furthermore, a given analysis (e.g., multiple regression) can be correctly employed to analyze data from numerous designs (e.g., a true experiment, a comparative design). A more useful distinction regarding types of evidence focuses not on the analysis, but on the design of the study yielding the evidence.

Correlational studies are quantitative, multi-subject designs in which participants have not been randomly assigned to treatment conditions. Analytic methods commonly (but not exclusively) applied with such designs are multiple regression analysis, canonical correlation analysis, hierarchical linear modeling, and structural equation modeling.

For example, as defined here, a correlational study might investigate differential achievement levels of students enrolled in classes of different sizes, where the students were not randomly assigned to classes of given sizes. Or researchers might collect data regarding the frequency with which teachers praise students, to examine relationships of these behaviors with students' self-concepts and school attendance.


Definitive causal conclusions in quantitative research can only be reached on the basis of true randomized trials. That is why it is so important for educational researchers to conduct more true experiments. Historically, randomization has been too infrequently invoked within the social sciences (Ludbrook & Dudley, 1998). However, for various reasons, evidence from types of research not involving randomized clinical trials is also relevant to evidence-based practice.

It is crucial to match research questions and research designs, and some questions are best addressed with nonexperimental designs. For example, questions involving school or classroom culture may require qualitative methods, and questions involving the intensive study of learning dynamics of individual children may require single-subject studies. Even when group quantitative methods are appropriate, randomized experiments may not be ideal if the immature state of knowledge on a given issue does not yet justify the expense of such trials. And in some cases clinical trials may raise ethical questions regarding denial of needed services to control group participants. Not all questions can be addressed with clinical trials, and unduly widespread use of clinical trials would also be undesirable because cross-contamination of effects across children involved in multiple experiments would then compromise all results.

Correlational designs do not provide the best evidence regarding causal mechanisms. Nevertheless, in at least two ways correlational evidence can be used to inform causal inferences and thus evidence-based practice. The first approach is statistically based, and involves statistically testing rival alternative causal models, even though the design is correlational. The second method is logic based and invokes logic and theory with nonexperimental data in an attempt to rule out all reasonable alternative explanations in support of making a single plausible causal inference.


The analytic methods that today we call structural equation modeling (SEM; or covariance structure analysis) originated in the work of Karl Joreskog (e.g., 1969, 1970, 1971, 1978), and the computer program, LISREL (i.e., analysis of Linear Structural Relationships) developed by Joreskog and his colleagues (e.g., Joreskog & Sorbom, 1989). These methods as originated in the 1960s and 1970s were then often called causal modeling, which hints at the potential of SEM to inform causal inferences.

SEM incorporates factor (or measurement) models, building on the factor analytic methods proposed by Spearman (1904), and a structural model linking these latent constructs, building on the path analytic methods proposed by Wright (1921, 1934). Within the structural model, analysts may test whether (a) two latent constructs (X and Y) covary or are correlated, (b) X causes Y, (c) Y causes X, or (d) X and Y reciprocally cause each other.

The appeal of SEM is that rival models can, and indeed should, be tested (see Thompson, 2000b). If only one of these four models fits the data (e.g., a model specifying that X causes Y), then there is at least some evidence bearing on the existence of a causal relationship.

For example, data reported by Bagozzi (1980) have been used in several reports to illustrate this application (see Joreskog & Sorbom, 1989, pp. 151-156, and Thompson, 1998b, pp. 37-39). Bagozzi's study investigated the job satisfaction and job performance of 122 workers. For these data, it appeared that a model positing that job performance leads to job satisfaction better fit the data than did models positing that job satisfaction leads to job performance or that satisfaction and performance are reciprocally related.


In some cases when true experiments are not performed, and even when structural modeling is not used, we still may be able to reach causal inferences with some degree of confidence. The capacity for extracting causal information from nonexperimental designs (e.g., intervention studies not invoking random assignment to groups) turns on our capacity to evaluate whether all relevant preintervention differences and design validity threats can be excluded (i.e., deemed essentially irrelevant).

For example, let's say two intact (i.e., not randomly assigned) groups of special education students were taught reading with two different curricula. We want to make some causal interpretation of the postintervention reading differences in the two conditions. We might investigate preintervention differences in the students on everything that we consider as being even potentially relevant (e.g., preintervention reading scores, socioeconomic status). We might also try to confirm that there were no meaningful extraneous contaminants of treatment influences (e.g., teachers had similar backgrounds in both conditions, curricula were implemented with fidelity). If we can rule out all such problems, we may have at least some plausible evidence that one curriculum is superior to the other curriculum, even though we have not performed a true experiment, and we have not statistically tested rival causal models.

The challenge to such efforts is that we may not be certain exactly which preintervention differences or what design validity threats are relevant in a given study. The beauty of true experiments is that the law of large numbers creates preintervention group equivalencies on all variables, even variables that we do not realize are essential to control.

But exclusion methods may be necessary in an environment where true experiments can not be used to address every important intervention question. And as our knowledge base grows, we may become more certain regarding which preintervention differences or treatment confounds are most noteworthy.


Both statistical modeling and logical exclusion methods require that models are "correctly specified." That is, the analytic results are sound only to the extent that

* All the correct variables, and only the correct variables, are employed within the tested models.

* The correct dynamics (e.g., mediation, moderation) are specified within the tested models (i.e., the correct analysis is used).

But as Pedhazur (1982) has noted, "The rub, however, is that the true model is seldom, if ever, known" (p. 229). And as Duncan (1975) has noted, "Indeed it would require no elaborate sophistry to show that we will never have the 'right' model in any absolute sense" (p. 101). Thus, both methods must be used cautiously in applying correlational evidence to help inform evidence-based practice. Nevertheless, correlation evidence, like other nonexperimental evidence, is relevant to evidence-based practice.


Educational research has sometimes been criticized for being poorly conducted (see Gall, Borg, & Gall, 1996, p. 151). For example, the National Academy of Science evaluated educational research generically and found "methodologically weak research, trivial studies, an infatuation with jargon, and a tendency toward fads with a consequent fragmentation of effort" (Atkinson & Jackson, 1992, p. 20). Nevertheless, even imperfect studies may provide some useful information. Few defects in published studies are sufficiently egregious to warrant total disqualification from any consideration.

A possible exception to this generalization encompasses studies using stepwise methods (Snyder, 1991). As Huberty (1994) noted, "It is quite common to find the use of 'stepwise analyses' reported in empirically based journal articles" (p. 261). Thompson (1995, 2001) explained that stepwise methods (a) do not correctly identify the best subset of predictors, (b) yield results that tend to be nonreplicable, and (c) "are positively satanic in their temptations toward Type I errors" (Cliff, 1987, p. 185), because most computer programs incorrectly compute the degrees of freedom for stepwise analyses. When researchers must select a subset of variables from a larger constellation of choices, the "all-possible-subsets" analyses described by Huberty (1994), and available in SAS, provide reasonable results.

The present article proposes some quality indicators for evaluating correlational research in efforts to inform evidence-based practice. Given the inherent challenges of educational research (Berliner, 2002), most studies are unavoidably imperfect and vary in the quality of the evidence they provide.

The quality indicators proposed are not new. But they may be insufficiently honored in contemporary analytic practice. For example, various effect size statistics have been proposed for decades (Huberty, 2002), but studies have shown effect sizes to be reported in less than half the published articles in various journals and various disciplines (see Thompson, 1999b; Vacha-Haase, Nilsson, Reetz, Lance, &, Thompson, 2000). Similarly, confidence intervals have been recommended for years (see Chandler, 1957), but empirical studies suggest that intervals are infrequently reported in published social science research (Kieffer, Reese, & Thompson, 2001).

The quality indicators presented are grouped into four sets: (a) measurement; (b) practical and clinical significance; (c) avoidance of some common analytic mistakes; and (d) confidence intervals for score reliability coefficients, statistics, and effect sizes. These are not the only indicator categories that might be identified, but the present categories will serve reasonably well to distinguish some recognizable features of correlational inquiry. Where space limitations preclude in-depth exploration of concerns, helpful references providing further elaboration are routinely provided.


The quality of the evidence informing practice is inherently limited by the psychometric integrity of the data being analyzed in a given study. Classically, measurement concerns are conceptualized as involving two primary considerations: score reliability and score validity. However, some modern measurement theories actually present a unified view of these concerns, such that reliability and validity issues are blended (Brennan, 2001).

Reliability can be conceptualized as addressing the question, "Do the scores measure anything?" (i.e., are nonrandom), and validity addresses the question, "Do the scores measure only the correct something that they are supposed to measure?" (Thompson, 2003). In this classical measurement view, reliability is a necessary but insufficient condition for validity.

Researchers have traditionally recognized that score validity is not immutable within a given measure; the same measure may yield scores valid for some purposes and respondents, and invalid for other inferences or respondents (Schmidt & Hunter, 1977). Lately, more researchers have come to realize in a similar vein that a given test also is not immutably reliable. As Wilkinson and the American Psychological Association (APA) Task Force on Statistical Inference (1999) recently emphasized:
 It is important to remember that a test is not reliable
 or unreliable.... Thus, authors should provide
 reliability coefficients of the scores for the
 data being analyzed even when the focus of their
 research is not psychometric. (p. 596)

Unfortunately, recent empirical studies of published research reports indicate that the vast preponderance of articles do not even mention reliability, much less report reliability for the data actually being analyzed (Vacha-Haase, Henson, & Caruso, 2002). These practices may originate in misconceptions that tests are reliable, and that once reliability has been established in a given sample, further concerns are moot (Thompson, 2003; Vacha-Haase, 1998).

A problematic practice is to "induct" the reliability coefficient from a prior study or a test manual (Vacha-Haase et al., 2002). Unfortunately, this induction of prior reliability coefficients turns on the premises that (a) the samples are comparable in their compositions and (b) the scores are roughly equivalent in their standard deviations across studies (Crocker & Algina, 1986, p. 144). Sadly, empirical studies suggest that such inductions are almost never explicitly justified and often are wildly inappropriate (Vacha-Haase, Kogan, &, Thompson, 2000; Whittington, 1998). It is unacceptable to induct the score reliability coefficients from prior studies or test manuals if there is no explicit evidence presented that the sample compositions and the standard deviations from the prior study and a current study are both reasonably comparable.

Quality Indicators:

* Score reliability coefficients are reported for all measured variables, based on induction from a prior study or test manual, with explicit and reasonable justifications as regards comparabilities of (a) sample compositions and (b) score dispersions.

* Score reliability coefficients are reported for all measured variables based on analysis of the data in hand in the particular study.

* Evidence is inducted, with explicit rationale, from a prior study or test manual that suggests scores are valid for the inferences being made in the study.

* Score validity is empirically evaluated based on data generated within the study.

* The influences of score reliability and validity on study interpretations are explicitly considered in reasonable detail.


Statistical significance estimates the probability, p, of sample results, given the sample size, and assuming the sample came from a population exactly described by the null hypothesis (Cohen, 1994; Thompson, 1996). In disciplines as diverse as wildlife sciences and psychology, the utility of statistical significance has been increasingly questioned in recent years (Anderson, Burnham, & Thompson, 2000; see Harlow, Mulaik, & Steiger, 1997 and Nickerson, 2000 for comprehensive summaries of both sides of the controversy). Indeed, a forthcoming issue of the Journal of Socio-Economics (see Thompson, in press-b) will include commentary by several economics Nobel laureates on this issue.

Practical significance evaluates the potential noteworthiness of study results, by quantifying the degree to which sample results diverge from the null hypothesis (Snyder & Lawson, 1993). These quantifications are often referred to generically as "effect sizes." There are literally dozens of effect size statistics (see Kirk, 1996). Many of these myriad choices can be arrayed within the following categories: (a) standardized differences (e.g., Cohen's d, Glass's [delta]), (b) "uncorrected" variance-accounted-for (e.g., [[eta].sup.2], [R.sup.2]), and (c) "corrected" variance-accounted-for (e.g., adjusted [R.sup.2], [[omega].sup.2]; see Thompson, 2002a). Thompson (in pressa), Kirk (1996), and Snyder and Lawson (1993) provide reviews on the numerous available choices.

Clinical significance evaluates the extent to which intervention recipients no longer meet diagnostic criteria (e.g., learning disability, depression), and, thus, no longer require specialized intervention (Jacobson, Roberts, Berns, & McGlinchey, 1999; Kendall, 1999). Clinical significance is potentially relevant only when the outcome variable can be interpreted using accepted diagnostic criteria (e.g., total cholesterol greater than 200 milligrams).

The fifth edition of the APA (2001) Publication Manual emphasized that
 It is almost always necessary to include some
 index of effect size or strength of relationship....
 The general principle to be followed ... is to provide
 the reader not only with information about
 statistical significance but also with enough information
 to assess the magnitude of the observed
 effect or relationship. (pp. 25-26,
 emphasis added)

The manual also describes failure to report effect sizes as "a defect" (p. 5). But the editors of 23 journals have gone beyond the APA Publication Manual and have published author guidelines requiring effect size reporting (Fidler, 2002).

Jacob Cohen, in his various books on power analysis, provided benchmarks for effect sizes that he deemed small, medium, and large. He formulated these based on his impressions of the range of effect sizes typical of the social science literature as a whole. He hesitated to provide such benchmarks because he felt that effects ought to be interpreted instead against the criteria of the researcher's values and related effects reported in prior literature. However, he provided these benchmarks of typicality because he felt that researchers would be more likely to report effect sizes if there were some standards for interpreting them, pending the reporting of effect sizes becoming routine within the literature. But "if people interpreted effect sizes [using fixed benchmarks] with the same rigidity that [alpha] = .05 has been used in statistical testing, we would merely be being stupid in another metric" (Thompson, 2001, pp. 82-83).

Glass, McGaw, and Smith (1981) argued that "there is no wisdom whatsoever in attempting to associate regions of the effect-size metric with descriptive adjectives such as 'small,' 'moderate,' 'large,' and the like" (p. 104). The only exception to this rule involves groundbreaking inquiry in which little or no previous research has been conducted, in which case Cohen's benchmarks may be useful as a (very) rough guide.

The problem is not the use of adjectives such as large or small. The problem is using fixed, generic benchmarks for making these judgments, rather than consulting the effects in related studies.

The results of a single study have meaning primarily as regards what they contribute to a literature, although, of course, the results of a single study sometimes do change thinking about a phenomenon (Thompson, in press-a). The comparison of effects against those reported in related prior studies enables researchers to evaluate the consistency of results across studies. This powerful view of all quantitative research as requiring "meta-analytic thinking" (Cumming & Finch, 2001; Thompson, 2002b) is promoted by interpreting results across studies. Such direct comparisons also alert researchers to inconsistent findings, which may highlight moderator variables or situations in which results vary across different subpopulations.


Even today when 23 journals (see McLean & Kaufman, 2000; Snyder, 2000) require effect size reporting, effect size reporting is more the exception than the norm (see Thompson, 1999b; Vacha-Haase, Nilsson et al., 2000). This does make it more difficult to interpret the effects in a given study in direct, explicit comparison with the effect sizes reported in prior studies, because effects must be computed or estimated for prior studies in which authors did not report effect sizes.

Effect sizes should be reported for all primary study outcomes, even when particular results are not statistically significant (Thompson, 2002b). Such reporting facilitates future meta-analytic integration of the study into the corpus of the literature.

Furthermore, some researchers do report, but do not interpret, their effect sizes (Vacha-Haase, Nilsson et al., 2000). Reporting, but not interpreting, effect sizes does not allow effect sizes to inform fully the interpretation of results.

A fundamental, but too common, mistake is failing to identify which effect size is being reported. Because there are so many different effect sizes (see Kirk, 1996), some with different ranges and properties, it is critical to identify reported effect statistics explicitly.

Finally, it is also important to recognize that effect sizes cannot magically escape the limitations or analytic assumptions of given analyses (Olejnik & Algina, 2000). These limitations and assumptions should be considered as part of result interpretation.

Quality Indicators:

* One or more effect size statistics is reported for each study primary outcome, and the effect statistic used is clearly identified.

* Authors interpret study effect sizes for selected practices by directly and explicitly comparing study effects with those reported in related prior studies.

* Authors explicitly consider study design and effect size statistic limitations as part of effect interpretation.


Across the literature a range of analytic errors are seen with some frequency. Some of these errors are unique to a particular method. For example, it is common for researchers to confuse descriptive discriminant analysis with predictive discriminant analysis, or vice versa, and consequently to misinterpret their discriminant analysis results (see Huberty, 1994; Kieffer et al., 2001). Other analytic errors occur generally across analytic choices.

Research evidence better informs practice when these errors are avoided. Here four such common generic, macro-analytic errors are noted. These can occur across two or more, or in some cases, all correlational analytic methods.


Throughout the general linear model (GLM), weights are either explicitly (e.g., regression, descriptive discriminant analysis) or implicitly (e.g., t-tests, ANOVA) applied to measured variables to estimate the scores on the latent variables that are actually the focus of the analysis (see Thompson, 2000a). These weights are given different names across analyses (e.g., beta weights, factor pattern coefficients, discriminant function coefficients), which has the effect of obfuscating the existence of the GLM.

When researchers obtain noteworthy effects, they commonly (and correctly) consult these weights as part of the process of determining the origins of detected effects. However, these weights are usually not correlation coefficients of predictors with outcome variables. In fact, a predictor may have the largest nonzero weight in an analysis even when the predictor is perfectly uncorrelated with the outcome variable (Thompson & Borrello, 1985).

Structure coefficients (i.e., correlations of measured variables with the latent variables actually being analyzed, such as regression ? scores) are also usually essential to correct interpretation (Courville & Thompson, 2001; Dunlap & Landis, 1998). For example, structure coefficients have been characterized as essential to the correct interpretation of multiple regression analysis (Courville & Thompson), exploratory factor analysis (Gorsuch, 1983, p. 207), confirmatory factor analysis (Graham, Guthrie, &, Thompson, 2003), descriptive discriminant analysis (Huberty, 1994), and canonical correlation analysis (Thompson, 1984).

Quality Indicators:

* GLM weights (e.g., beta weights) are interpreted as reflecting correlations of predictors with outcome variables only in the exceptional case that the weights indeed are correlation coefficients.

* When noteworthy results are detected, and the origins of these effects are investigated, the interpretation includes examination of structure coefficients.


It is not uncommon (Pedhazur, 1982, pp. 452-453) to see researchers convert one or more of their independent or predictor variables into nominal scale in order to run OVA methods (e.g., ANOVA). For example, researchers may take intervally-scaled pretest data (e.g., IQ scores, pretest achievement scores) and characterize participants as either "low" or "high" in learning aptitude.

Such dichotomization (trichotomization, etc.) (a) "throws information away" (i.e., discards score variability; Kerlinger, 1986, p. 558); (b) attenuates reliability of the scores being analyzed; (c) distorts variable distributions; and (d) distorts relationships among variables (Thompson, 1986). The result is analyses that are ecologically less valid.

In her comprehensive Monte Carlo study, Hester (2000) provided considerably more detail on the consequences of such ill-considered analytic choices. The consequences of these conversions are particularly deleterious for building an integrated literature when different researchers use divergent cutoffs (e.g., different sample-specific median splits) to implement the conversions. For example, if researcher Jones dichotomizes pretest IQ data at Jones's sample median of 95, and researcher Smith does so at Smith's sample median of 105, we will never know whether discrepant ANOVA or MANOVA results are (a) an artifact of using different cutpoints to dichotomize, or (b) a failure to replicate results.

Quality Indicator:

* Interval data are not converted to nominal scale, unless such choices are justified on the extraordinary basis of distribution shapes, and the consequences of the conversion are thoughtfully considered as part of result interpretation.


Univariate methods (i.e., analyses using a single dependent variable) are quite commonly used in educational research (Kieffer et al., 2001). These methods can be quite appropriate for some studies. However, there are two situations in which univariate methods are inappropriate.

First, univariate methods are generally inappropriate in the presence of multiple outcomes variables. The use of univariate methods when a study involves several outcome variables (a) inflates the probability of experimentwise Type I errors, and (b) does not honor the reality that outcome variables can interact with each other to define unique outcomes that are more than their constituent parts (Fish, 1988).

Regarding the second concern, Thompson (1999a) provided a heuristic data set illustrating the importance of these issues. In his example data set, the two means on X and Y did not differ to a statistically significant degree (both ANOVA p values were .774), and furthermore the ANOVA [eta.sup.2] effect sizes were both computed to be 0.469%. Thus, the two sets of ANOVA results were not statistically significant, and they both involved extremely small effect sizes. However, a MANOVA/descriptive discriminant analysis (DDA) of the same data yielded a PCALCULATED value of .0002, and a multivariate [eta.sup.2] of 62.5%!

This means that the Bonferroni correction in the presence of several or many outcome variables is not suitable, for two reasons. First, the correction lowers power against Type II error. Second, multiple univariate analyses do not honor the ecological reality that all the variables, including the outcomes, can interact with each other to create unique effects that will only be discovered in a multivariate analysis.

Second, the use of univariate methods (e.g., ANOVA) post hoc to multivariate tests is inappropriate, albeit common (Kieffer et al., 2001). Put simply, a MANOVA and several ANOVAs each using the same measured outcome variables test completely different and irreconcilable effects, because the ANOVAs do not consider the relationships among the outcomes. These relationships are an essential consideration in the multivariate analyses, as illustrated in the Thompson (1999a) heuristic example.

In the words of Borgen and Seling (1978), "When data truly are multivariate, as implied by the application of MANOVA, a multivariate follow-up technique seems necessary to 'discover' the complexity of the data" (p. 696). It is illogical to first declare interest in a multivariate omnibus system of variables, and then to explore detected effects in this multivariate world by conducting nonmultivariate tests.

A logical MANOVA post hoc method is descriptive discriminant analysis, which Huberty (1994) noted is "closely aligned to the study of effects determined by a multivariate analysis of variance (MANOVA)" (p. 30). Huberty (1994) provided several chapters on using DDA post hoc to MANOVA to assess and describe multivariate dynamics.

Quality Indicators:

* Univariate methods are not used in the presence of multiple outcome variables.

* Univariate methods are not used post hoc to multivariate tests.


All statistical methods require that certain assumptions (e.g., homogeneity of variance in ANOVA, homogeneity of regression slopes in ANCOVA) must be met in order for p values and effect sizes to be accurate. Methodological assumptions are never perfectly met, but must be at least approximately met in order for results to be approximately correct.

Empirical studies of published articles suggest that statistical assumptions are too rarely tested by researchers (Keselman et al., 1998). These assumptions are more important than many researchers may realize, as suggested by Wilcox (1998) in his article titled, "How many discoveries have been lost by ignoring modern statistical methods?"

Statistical assumptions can be particularly important when statistical corrections are invoked, as in ANCOVA, particularly when used with nonrandom intact intervention groups (see Thompson, 1992). Using ANCOVA when the homogeneity of regression assumption is not met leads to "tragically misleading analyses" that actually "can mistakenly make compensatory education look harmful" (Campbell & Erlebacher, 1975, p. 597).

Quality Indicator:

* Persuasive evidence is explicitly presented that the assumptions of statistical methods are sufficiently well-met for results to be deemed credible.


Confidence intervals (CIs) can be used to determine whether a given null hypothesis would be rejected. If a hypothesized value (e.g., r = 0; r = .5) is not within the interval, the null hypothesis positing the parameter value is rejected. However, this use of confidence intervals does not tap the primary positive features of using confidence intervals (Thompson, 1998a, 2001).

Confidence intervals inform judgment regarding all the values of the parameter that appear to be plausible, given the data (Cumming & Finch, 2001). Thus, by comparing the overlaps of confidence intervals across studies, researchers can evaluate the consistency of evidence across studies (Thompson, 2002b).

The widths of confidence intervals within a study, or across studies, also provide critical information regarding the precision of estimates in a study or in a literature. When intervals are wide, the evidence for a given point estimate being correct is called into question. Researchers may over-interpret effects in a literature and not recognize the imprecision of a body of literature, unless confidence intervals are computed and directly compared across studies.

For these various reasons, confidence intervals are increasingly recognized as being "in general, the best reporting strategy" and "the use of confidence intervals is therefore strongly recommended' (American Psychological Association, 2001, p. 22, emphasis added). Of course, as Fidler, Thomason, Cumming, Finch, and Leeman (2004) pointed out, as with any other statistical methods, CIs are not a panacea, and can be used thoughtlessly.


Some researchers misinterpret confidence intervals as telling us how confident we may be (e.g., 95%) that a given, single interval captures a population parameter, such as a correlational effect size (e.g., r, [r.sup.2]). However, the confidence statements when dealing with confidence intervals are about a large or infinite set of intervals drawn from a population capturing the interval a given percentage (e.g., 95%) of the time, and these confidence statements are not about single intervals (Thompson, 2002b).

We never know, unless we have the population data (and then would not be computing a CI), whether our single interval does or does not capture a population parameter. The probabilities of intervals capturing the population parameter (e.g., r, [r.sup.2]) may be different even for a series of 95% confidence intervals.

Confidence intervals can be computed for (a) reliability coefficients (Fan & Thompson, 2001); (b) sample statistics (e.g., M, r); and (c) effect sizes (Thompson, 2002b). CIs are so appealing because using intervals across studies will ultimately lead us to the correct population value, even if our initial expectations are wildly in error (Schmidt, 1996)! Software for computing confidence intervals for effect sizes is widely available (Algina & Keselman, 2003; Cumming & Finch, 2001; Smithson, 2001; Steiger & Fouladi, 1992). Kline's (2004) recent book provides a comprehensive tutorial.

Quality Indicators:

* Confidence intervals are reported for the reliability coefficients derived for study data.

* Confidence intervals are reported for the sample statistics (e.g., means, correlation coefficients) of primary interest in the study.

* Confidence intervals are reported for study effect sizes.

* Confidence intervals are interpreted by direct and explicit comparison with related CIs from prior studies.


Within the quantitative group-design genre, only true experiments offer definitive evidence for causal inferences that can inform evidence-based instructional practice. But not all educational interventions are readily amenable to experiments. In addition, experimental studies of educational interventions are compromised by cross-contamination when students participate in multiple interventions.

In such cases correlational evidence may be useful in adducing complementary evidence. Correlational studies can produce intriguing results that are then subjected to experimental study. And correlational evidence can at least tentatively inform evidence-based practice when sophisticated causal modeling (e.g., regression discontinuity analyses) or exclusion methods are employed. Correlational evidence is most informative when exemplary practices are followed with regard to (a) measurement, (b) quantifying effects, (c) avoidance of common macro-analytic errors, and (d) use of confidence intervals to portray the consistency of possible effects and the precisions of the effect estimates. Table 1 presents a list of the quality indicators suggested for research in this genre.
Suggested Quality Indicators for Correlational Research


1. Score reliability coefficients are reported for all
measured variables, based on induction from a
prior study or test manual, with explicit and reasonable
justifications as regards comparabilities of
(a) sample compositions and (b) score dispersions.

2. Score reliability coefficients are reported for all
measured variables, based on analysis of the data
in hand in the particular study.

3. Evidence is inducted, with explicit rationale, from
a prior study or test manual that suggests scores
are valid for the inferences being made in the

4. Score validity is empirically evaluated based on
data generated within the study.

5. The influences of score reliability and validity on
study interpretations are explicitly considered in
reasonable detail.

Practical and Clinical Significance

6. One or more effect size statistics is reported for
each study primary outcome, and the effect statistic
used is clearly identified.

7. Authors interpret study effect sizes for selected
practices by directly and explicitly comparing
study effects with those reported in related prior

8. Authors explicitly consider study design and effect
size statistic limitations as part of effect interpretation.

Avoiding Some Common Macro-Analytic Mistakes

9. GLM weights (e.g., beta weights) are interpreted
as reflecting correlations of predictors with outcome
variables only in the exceptional case that
the weights indeed are correlation coefficients.

10. When noteworthy results are detected, and the
origins of these effects are investigated, the interpretation
includes examination of structure coefficients.

11. Interval data are not converted to nominal scale,
unless such choices are justified on the extraordinary
basis of distribution shapes, and the consequences
of the conversion are thoughtfully
considered as part of result interpretation.

12. Univariate methods are not used in the presence
of multiple outcome variables.

13. Univariate methods are not used post hoc to multivariate

14. Persuasive evidence is explicitly presented that the
assumptions of statistical methods are sufficiently
well-met for results to be deemed credible.

CIs for Reliability Coefficients, Statistics, and Effect Sizes

15. Confidence intervals are reported for the reliability
coefficients derived for study data.

16. Confidence intervals are reported for the sample
statistics (e.g., means, correlation coefficients) of
primary interest in the study.

17. Confidence intervals are reported for study effect

18. Confidence intervals are interpreted by direct and
explicit comparison with related CIs from prior


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BRUCE THOMPSON (CEC TX Federation), Texas A & M University and Baylor College of Medicine, College Station, Texas. KAREN E. DIAMOND (CEC IN Federation), Professor and Director, Child Development Laboratory School, Purdue University, W. Lafayette, Indiana. ROBIN MCWILLIAM, Director, Center for Child Development, Professor of Pediatrics and Special Education, Vanderbilt University Medical Center, Nashville, Tennessee. PATRICIA SNYDER (CEC #514), Associate Dean for Research and Graduate Studies, Louisiana State University Health Science Center, New Orleans. SCOTT W. SNYDER (CEC #144), School of Education Dean's Office, University of Alabama, Birmingham.

Correspondence concerning this article should be addressed to Bruce Thompson, TAMU Department of Educational Psychology, Texas A&M University, College Station, TX 77843-4225, or via e-mail using the Internet URL:

Manuscript received January 2004; accepted April 2004.

BRUCE THOMPSON Texas A&M University and Baylor College of Medicine

KAREN E. DIAMOND Purdue University

ROBIN MCWILLIAM Vanderbilt University

PATRICIA SNYDER Louisiana State University Health Science Center

SCOTT W. SNYDER University of Alabama
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Date:Jan 1, 2005
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