In Meta-Analyses, Weak Inclusion Standards Lead to Misleading Conclusions. Here’s Proof.

By Robert Slavin and Amanda Neitzel, Johns Hopkins University

In two recent blogs (here and here), I’ve written about Baltimore’s culinary glories: crabs and oysters. My point was just that in both cases, there is a lot you have to discard to get to what matters. But I was of course just setting the stage for a problem that is deadly serious, at least to anyone concerned with evidence-based reform in education.

Meta-analysis has contributed a great deal to educational research and reform, helping readers find out about the broad state of the evidence on practical approaches to instruction and school and classroom organization. Recent methodological developments in meta-analysis and meta-regression, and promotion of the use of these methods by agencies such as IES and NSF, have expanded awareness and use of modern methods.

Yet looking at large numbers of meta-analyses published over the past five years, even up to the present, the quality is highly uneven. That’s putting it nicely.  The problem is that most meta-analyses in education are far too unselective with regards to the methodological quality of the studies they include. Actually, I’ve been ranting about this for many years, and along with colleagues, have published several articles on it (e.g., Cheung & Slavin, 2016; Slavin & Madden, 2011; Wolf et al., 2020). But clearly, my colleagues and I are not making enough of a difference.

My colleague, Amanda Neitzel, and I thought of a simple way we could communicate the enormous difference it makes if a meta-analysis accepts studies that contain design elements known to inflate effect sizes. In this blog, we once again use the Kulik & Fletcher (2016) meta-analysis of research on computerized intelligent tutoring, which I critiqued in my blog a few weeks ago (here). As you may recall, the only methodological inclusion standards used by Kulik & Fletcher required that studies use RCTs or QEDs, and that they have a duration of at least 30 minutes (!!!). However, they included enough information to allow us to determine the effect sizes that would have resulted if they had a) weighted for sample size in computing means, which they did not, and b) excluded studies with various features known to inflate effect size estimates. Here is a table summarizing our findings when we additionally excluded studies containing procedures known to inflate mean effect sizes:

If you follow meta-analyses, this table should be shocking. It starts out with 50 studies and a very large effect size, ES=+0.65. Just weighting the mean for study sample sizes reduces this to +0.56. Eliminating small studies (n<60) cut the number of studies almost in half (n=27) and cut the effect size to +0.39. But the largest reductions are due to excluding “local” measures, which on inspection are always measures made by developers or researchers themselves. (The alternative was “standardized measures.”) By itself, excluding local measures (and weighting) cut the number of included studies to 12, and the effect size to +0.10, which was not significantly different from zero (p=.17). Excluding small, brief, and “local” measures only slightly changes the results, because both small and brief studies almost always use “local” (i.e., researcher-made) measures. Excluding all three, and weighting for sample size, leaves this review with only nine studies and an effect size of +0.09, which is not significantly different from zero (p=.21).

The estimates at the bottom of the chart represent what we call “selective standards.” These are the standards we apply in every meta-analysis we write (see www.bestevidence.org), and in Evidence for ESSA (www.evidenceforessa.org).

It is easy to see why this matters. Selective standards almost always produce much lower estimates of effect sizes than do reviews with much less selective standards, which therefore include studies containing design features that have a strong positive bias on effect sizes. Consider how this affects mean effect sizes in meta-analyses. For example, imagine a study that uses two measures of achievement. One is a measure made by the researcher or developer specifically to be “sensitive” to the program’s outcomes. The other is a test independent of the program, such as GRADE/GMADE or Woodcock, standardized tests but not necessarily state tests. Imagine that the researcher-made measure obtains an effect size of +0.30, while the independent measure has an effect size of +0.10. A less-selective meta-analysis would report a mean effect size of +0.20, a respectable-sounding impact. But a selective meta-analysis would report an effect size of +0.10, a very small impact. Which of these estimates represents an outcome with meaning for practice? Clearly, school leaders should not value the +0.30 or +0.20 estimates, which require use of a test designed to be “sensitive” to the treatment. They should care about the gains on the independent test, which represents what educators are trying to achieve and what they are held accountable for. The information from the researcher-made test may be valuable to the researchers, but it has little or no value to educators or students.

The point of this exercise is to illustrate that in meta-analyses, choices of methodological exclusions may entirely determine the outcomes. Had they chosen other exclusions, the Kulik & Fletcher meta-analysis could have reported any effect size from +0.09 (n.s.) to +0.65 (p<.000).

The importance of these exclusions is not merely academic. Think how you’d explain the chart above to your sister the principal:

            Principal Sis: I’m thinking of using one of those intelligent tutoring programs to improve achievement in our math classes. What do you suggest?

            You:  Well, it all depends. I saw a review of this in the top journal in education research. It says that if you include very small studies, very brief studies, and studies in which the researchers made the measures, you could have an effect size of +0.65! That’s like seven additional months of learning!

            Principal Sis:  I like those numbers! But why would I care about small or brief studies, or measures made by researchers? I have 500 kids, we teach all year, and our kids have to pass tests that we don’t get to make up!

            You (sheepishly):  I guess you’re right, Sis. Well, if you just look at the studies with large numbers of students, which continued for more than 12 weeks, and which used independent measures, the effect size was only +0.09, and that wasn’t even statistically significant.

            Principal Sis:  Oh. In that case, what kinds of programs should we use?

From a practical standpoint, study features such as small samples or researcher-made measures add a lot to effect sizes while adding nothing to the value to students or schools of the programs or practices they want to know about. They just add a lot of bias. It’s like trying to convince someone that corn on the cob is a lot more valuable than corn off the cob, because you get so much more quantity (by weight or volume) for the same money with corn on the cob.     Most published meta-analyses only require that studies have control groups, and some do not even require that much. Few exclude researcher- or developer-made measures, or very small or brief studies. The result is that effect sizes in published meta-analyses are very often implausibly large.

Meta-analyses that include studies lacking control groups or studies with small samples, brief durations, pretest differences, or researcher-made measures report overall effect sizes that cannot be fairly compared to other meta-analyses that excluded such studies. If outcomes do not depend on the power of the particular program but rather on the number of potentially biasing features they did or did not exclude, then outcomes of meta-analyses are meaningless.

It is important to note that these two examples are not at all atypical. As we have begun to look systematically at published meta-analyses, most of them fail to exclude or control for key methodological factors known to contribute a great deal of bias. Something very serious has to be done to change this. Also, I’d remind readers that there are lots of programs that do meet strict standards and show positive effects based on reality, not on including biasing factors. At www.evidenceforessa.org, you can see more than 120 reading and math programs that meet selective standards for positive impacts. The problem is that in meta-analyses that include studies containing biasing factors, these truly effective programs are swamped by a blizzard of bias.

In my recent blog (here) I proposed a common set of methodological inclusion criteria that I would think most methodologists would agree to.  If these (or a similar consensus list) were consistently used, we could make more valid comparisons both within and between meta-analyses. But as long as inclusion criteria remain highly variable from meta-analysis to meta-analysis, then all we can do is pick out the few that do use selective standards, and ignore the rest. What a terrible waste.

References

Cheung, A., & Slavin, R. (2016). How methodological features affect effect sizes in education. Educational Researcher, 45 (5), 283-292.

Kulik, J. A., & Fletcher, J. D. (2016). Effectiveness of intelligent tutoring systems: a meta-analytic review. Review of Educational Research, 86(1), 42-78.

Slavin, R. E., Madden, N. A. (2011). Measures inherent to treatments in program effectiveness reviews. Journal of Research on Educational Effectiveness, 4, 370–380.

Wolf, R., Morrison, J.M., Inns, A., Slavin, R. E., & Risman, K. (2020). Average effect sizes in developer-commissioned and independent evaluations. Journal of Research on Educational Effectiveness. DOI: 10.1080/19345747.2020.1726537

Photo credit: Deeper Learning 4 All, (CC BY-NC 4.0)

This blog was developed with support from Arnold Ventures. The views expressed here do not necessarily reflect those of Arnold Ventures.

Note: If you would like to subscribe to Robert Slavin’s weekly blogs, just send your email address to thebee@bestevidence.org. 

How Can You Tell When The Findings of a Meta-Analysis Are Likely to Be Valid?

In Baltimore, Faidley’s, founded in 1886, is a much loved seafood market inside Lexington Market. Faidley’s used to be a real old-fashioned market, with sawdust on the floor and an oyster bar in the center. People lined up behind their favorite oyster shucker. In a longstanding tradition, the oyster shuckers picked oysters out of crushed ice and tapped them with their oyster knives. If they sounded full, they opened them. But if they did not, the shuckers discarded them.

I always noticed that the line was longer behind the shucker who was discarding the most oysters. Why? Because everyone knew that the shucker who was pickier was more likely to come up with a dozen fat, delicious oysters, instead of say, nine great ones and three…not so great.

I bring this up today to tell you how to pick full, fair meta-analyses on educational programs. No, you can’t tap them with an oyster knife, but otherwise, the process is similar. You want meta-analysts who are picky about what goes into their meta-analyses. Your goal is to make sure that a meta-analysis produces results that truly represent what teachers and schools are likely to see in practice when they thoughtfully implement an innovative program. If instead you pick the meta-analysis with the biggest effect sizes, you will always be disappointed.

As a special service to my readers, I’m going to let you in on a few trade secrets about how to quickly evaluate a meta-analysis in education.

One very easy way to evaluate a meta-analysis is to look at the overall effect size, probably shown in the abstract. If the overall mean effect size is more than about +0.40, you probably don’t have to read any further. Unless the treatment is tutoring or some other treatment that you would expect to make a massive difference in student achievement, it is rare to find a single legitimate study with an effect size that large, much less an average that large. A very large effect size is almost a guarantee that a meta-analysis is full of studies with design features that greatly inflate effect sizes, not studies with outstandingly effective treatments.

Next, go to the Methods section, which will have within it a section on inclusion (or selection) criteria. It should list the types of studies that were or were not accepted into the study. Some of the criteria will have to do with the focus of the meta-analysis, specifying, for example, “studies of science programs for students in grades 6 to 12.” But your focus is on the criteria that specify how picky the meta-analysis is. As one example of a picky set of critera, here are the main ones we use in Evidence for ESSA and in every analysis we write:

1. Studies had to use random assignment or matching to assign students to experimental or control groups, with schools and students in each specified in advance.
2. Students assigned to the experimental group had to be compared to very similar students in a control group, which uses business-as-usual. The experimental and control students must be well matched, within a quarter standard deviation at pretest (ES=+0.25), and attrition (loss of subjects) must be no more than 15% higher in one group than the other at the end of the study. Why? It is essential that experimental and control groups start and remain the same in all ways other than the treatment. Controls for initial differences do not work well when the differences are large.
3. There must be at least 30 experimental and 30 control students. Analyses of combined effect sizes must control for sample sizes. Why? Evidence finds substantial inflation of effect sizes in very small studies.
4. The treatments must be provided for at least 12 weeks. Why? Evidence finds major inflation of effect sizes in very brief studies, and brief studies do not represent the reality of the classroom.
5. Outcome measures must be measures independent of the program developers and researchers. Usually, this means using national tests of achievement, though not necessarily standardized tests. Why? Research has found that tests made by researchers can inflate effect sizes by double, or more, and research-made measures do not represent the reality of classroom assessment.

There may be other details, but these are the most important. Note that there is a double focus of these standards. Each is intended both to minimize bias, but also to maximize similarity to the conditions faced by schools. What principal or teacher who cares about evidence would be interested in adopting a program evaluated in comparison to a very different control group? Or in a study with few subjects, or a very brief duration? Or in a study that used measures made by the developers or researchers? This set is very similar to what the What Works Clearinghouse (WWC) requires, except #5 (the WWC requires exclusion of “overaligned” measures, but not developer-/researcher-made measures).

If these criteria are all there in the “Inclusion Standards,” chances are you are looking at a top-quality meta-analysis. As a rule, it will have average effect sizes lower than those you’ll see in reviews without some or all of these standards, but the effect sizes you see will probably be close to what you will actually get in student achievement gains if your school implements a given program with fidelity and thoughtfulness.

What I find astonishing is how many meta-analyses do not have standards this high. Among experts, these criteria are not controversial, except for the last one, which shouldn’t be. Yet meta-analyses are often written, and accepted by journals, with much lower standards, thereby producing greatly inflated, unrealistic effect sizes.

As one example, there was a meta-analysis of Direct Instruction programs in reading, mathematics, and language, published in the Review of Educational Research (Stockard et al., 2016). I have great respect for Direct Instruction, which has been doing good work for many years. But this meta-analysis was very disturbing.

The inclusion and exclusion criteria in this meta-analysis did not require experimental-control comparisons, did not require well-matched samples, and did not require any minimum sample size or duration. It was not clear how many of the outcomes measures were made by program developers or researchers, rather than independent of the program.

With these minimal inclusion standards, and a very long time span (back to 1966), it is not surprising that the review found a great many qualifying studies. 528, to be exact. The review also reported extraordinary effect sizes: +0.51 for reading, +0.55 for math, and +0.54 for language. If these effects were all true and meaningful, it would mean that DI is much more effective than one-to-one tutoring, for example.

But don’t get your hopes up. The article included an online appendix that showed the sample sizes, study designs, and outcomes of every study.

First, the authors identified eight experimental designs (plus single-subject designs, which were treated separately). Only two of these would meet anyone’s modern standards of meta-analysis: randomized and matched. The others included pre-post gains (no control group), comparisons to test norms, and other pre-scientific designs.

Sample sizes were often extremely small. Leaving aside single-case experiments, there were dozens of single-digit sample sizes (e.g., six students), often with very large effect sizes. Further, there was no indication of study duration.

What is truly astonishing is that RER accepted this study. RER is the top-rated journal in all of education, based on its citation count. Yet this review, and the Kulik & Fletcher (2016) review I cited in a recent blog, clearly did not meet minimal standards for meta-analyses.

My colleagues and I will be working in the coming months to better understand what has gone wrong with meta-analysis in education, and to propose solutions. Of course, our first step will be to spend a lot of time at oyster bars studying how they set such high standards. Oysters and beer will definitely be involved!

Photo credit: Annette White / CC BY-SA (https://creativecommons.org/licenses/by-sa/4.0)

References

Kulik, J. A., & Fletcher, J. D. (2016). Effectiveness of intelligent tutoring systems: a meta-analytic review. Review of Educational Research, 86(1), 42-78.

Stockard, J., Wood, T. W., Coughlin, C., & Rasplica Khoury, C. (2018). The effectiveness of Direct Instruction curricula: A meta-analysis of a half century of research. Review of Educational Research, 88(4), 479–507. https://doi.org/10.3102/0034654317751919

This blog was developed with support from Arnold Ventures. The views expressed here do not necessarily reflect those of Arnold Ventures.

Note: If you would like to subscribe to Robert Slavin’s weekly blogs, just send your email address to thebee@bestevidence.org. 

Meta-Analysis or Muddle-Analysis?

One of the best things about living in Baltimore is eating steamed hard shell crabs every summer.  They are cooked in a very spicy mix of spices, and with Maryland corn and Maryland beer, these define the very peak of existence for Marylanders.  (To be precise, the true culture of the crab also extends into Virginia, but does not really exist more than 20 miles inland from the bay).  

As every crab eater knows, a steamed crab comes with a lot of inedible shell and other inner furniture.  So you get perhaps an ounce of delicious meat for every pound of whole crab. Here is a bit of crab math.  Let’s say you have ten pounds of whole crabs, and I have 20 ounces of delicious crabmeat.  Who gets more to eat?  Obviously I do, because your ten pounds of crabs will only yield 10 ounces of meat. 

How Baltimoreans learn about meta-analysis.

All Baltimoreans instinctively understand this from birth.  So why is this same principle not understood by so many meta-analysts?

I recently ran across a meta-analysis of research on intelligent tutoring programs by Kulik & Fletcher (2016),  published in the Review of Educational Research (RER). The meta-analysis reported an overall effect size of +0.66! Considering that the single largest effect size of one-to-one tutoring in mathematics was “only” +0.31 (Torgerson et al., 2013), it is just plain implausible that the average effect size for a computer-assisted instruction intervention is twice as large. Consider that a meta-analysis our group did on elementary mathematics programs found a mean effect size of +0.19 for all digital programs, across 38 rigorous studies (Slavin & Lake, 2008). So how did Kulik & Fletcher come up with +0.66?

The answer is clear. The authors excluded very few studies except for those of less than 30 minutes’ duration. The studies they included used methods known to greatly inflate effect sizes, but they did not exclude or control for them. To the authors’ credit, they then carefully documented the effects of some key methodological factors. For example, they found that “local” measures (presumably made by researchers) had a mean effect size of +0.73, while standardized measures had an effect size of +0.13, replicating findings of many other reviews (e.g., Cheung & Slavin, 2016). They found that studies with sample sizes less than 80 had an effect size of +0.78, while those with samples of more than 250 had an effect size of +0.30. Brief studies had higher effect sizes than those of longer studies, as found in many studies. All of this is nice to know, but even knowing it all, Kulik & Fletcher failed to control for any of it, not even to weight by sample size. So, for example, the implausible mean effect size of +0.66 includes a study with a sample size of 33, a duration of 80 minutes, and an effect size of +1.17, on a “local” test. Another had 48 students, a duration of 50 minutes, and an effect size of +0.95. Now, if you believe that 80 minutes on a computer is three times as effective for math achievement than months of one-to-one tutoring by a teacher, then I have a lovely bridge in Baltimore I’d like to sell you.

I’ve long been aware of these problems with meta-analyses that neither exclude nor control for characteristics of studies known to greatly inflate effect sizes. This was precisely the flaw for which I criticized John Hattie’s equally implausible reviews. But what I did not know until recently was just how widespread this is.

I was working on a proposal to do a meta-analysis of research on technology applications in mathematics. A colleague located every meta-analysis published on this topic since 2013. She found 20 of them. After looking at the remarkable outcomes on a few, I computed a median effect size across all twenty. It was +0.44. That is, to put it mildly, implausible. Looking further, I discovered that only one of the reviews adjusted for sample size (inverse variances). Its mean effect size was +0.05. Every one of the other 19 meta-analyses, all in respectable journals, did not control for methodological features or exclude studies based on them, and reported effect sizes up to +1.02 and +1.05.

Meta-analyses are important, because they are widely read and widely cited, in comparison to individual studies. Yet until meta-analyses start consistently excluding, or at least controlling for studies with factors known to inflate mean effect sizes, then they will have little if any meaning for practice. As things stand now, the overall mean impacts reported by meta-analyses in education depend on how stringent the inclusion standards were, not how effective the interventions truly were.

This is a serious problem for evidence-based reform. Our field knows how to solve it, but all too many meta-analysts do not do so. This needs to change. We see meta-analyses claiming huge impacts, and then wonder why these effects do not transfer to practice. In fact, these big effect sizes do not transfer because they are due to methodological artifacts, not to actual impacts teachers are likely to obtain in real schools with real students.

Ten pounds (160 ounces) of crabs only appear to be more than 20 ounces of crabmeat,  because the crabs contain a lot you need to discard.  The same is true of meta-analyses.  Using small samples, brief durations, and researcher-made measures in evaluations inflate effect sizes without adding anything to the actual impact of treatments for students.  Our job as meta-analysts is to strip away the bias the best we can, and get to the actual impact.  Then we can make comparisons and generalizations that make sense, and move forward understanding of what really works in education.

In our research group, when we deal with thorny issues of meta-analysis, I often ask my colleagues to consider that they had a sister who is a principal.  “What would you say to her,” I ask, “if she asked what really works, all BS aside?  Would you suggest a program that was very effective in a 30-minute study?  One that has only been evaluated with 20 students?  One that has only been shown to be effective if the researcher gets to make the measure?  Principals are sharp, and appropriately skeptical.  Your sister would never accept such evidence.  Especially if she’s experienced with Baltimore crabs.”

References

Cheung, A., & Slavin, R. (2016). How methodological features affect effect sizes in education. Educational Researcher, 45 (5), 283-292.

Kulik, J. A., & Fletcher, J. D. (2016). Effectiveness of intelligent tutoring systems: a meta-analytic review. Review of Educational Research, 86(1), 42-78.

Slavin, R., & Lake, C. (2008). Effective programs in elementary mathematics: A best-evidence synthesis. Review of Educational Research, 78 (3), 427-515.

Torgerson, C. J., Wiggins, A., Torgerson, D., Ainsworth, H., & Hewitt, C. (2013). Every Child Counts: Testing policy effectiveness using a randomised controlled trial, designed, conducted and reported to CONSORT standards. Research In Mathematics Education, 15(2), 141–153. doi:10.1080/14794802.2013.797746.

Photo credit: Kathleen Tyler Conklin/(CC BY 2.0)

This blog was developed with support from Arnold Ventures. The views expressed here do not necessarily reflect those of Arnold Ventures.

Note: If you would like to subscribe to Robert Slavin’s weekly blogs, just send your email address to thebee@bestevidence.org. 

Even Magic Johnson Sometimes Had Bad Games: Why Research Reviews Should Not Be Limited to Published Studies

When my sons were young, they loved to read books about sports heroes, like Magic Johnson. These books would all start off with touching stories about the heroes’ early days, but as soon as they got to athletic feats, it was all victories, against overwhelming odds. Sure, there were a few disappointments along the way, but these only set the stage for ultimate triumph. If this weren’t the case, Magic Johnson would have just been known by his given name, Earvin, and no one would write a book about him.

Magic Johnson was truly a great athlete and is an inspiring leader, no doubt about it. However, like all athletes, he surely had good days and bad ones, good years and bad. Yet the published and electronic media naturally emphasize his very best days and years. The sports press distorts the reality to play up its heroes’ accomplishments, but no one really minds. It’s part of the fun.

In educational research evaluating replicable programs and practices, our objectives are quite different. Sports reporting builds up heroes, because that’s what readers want to hear about. But in educational research, we want fair, complete, and meaningful evidence documenting the effectiveness of practical means of improving achievement or other outcomes. The problem is that academic publications in education also distort understanding of outcomes of educational interventions, because studies with significant positive effects (analogous to Magic’s best days) are far more likely to be published than are studies with non-significant differences (like Magic’s worst days). Unlike the situation in sports, these distortions are harmful, usually overstating the impact of programs and practices. Then when educators implement interventions and fail to get the results reported in the journals, this undermines faith in the entire research process.

It has been known for a long time that studies reporting large, positive effects are far more likely to be published than are studies with smaller or null effects. One long-ago study, by Atkinson, Furlong, & Wampold (1982), randomly assigned APA consulting editors to review articles that were identical in all respects except that half got versions with significant positive effects and half got versions with the same outcomes but marked as not significant. The articles with outcomes marked “significant” were twice as likely as those marked “not significant” to be recommended for publication. Reviewers of the “significant” studies even tended to state that the research designs were excellent much more often than did those who reviewed the “non-significant” versions.

Not only do journals tend not to accept articles with null results, but authors of such studies are less likely to submit them, or to seek any sort of publicity. This is called the “file-drawer effect,” where less successful experiments disappear from public view (Glass et al., 1981).

The combination of reviewers’ preferences for significant findings and authors’ reluctance to submit failed experiments leads to a substantial bias in favor of published vs. unpublished sources (e.g., technical reports, dissertations, and theses, often collectively termed “gray literature”). A review of 645 K-12 reading, mathematics, and science studies by Cheung & Slavin (2016) found almost a two-to-one ratio of effect sizes between published and gray literature reports of experimental studies, +0.30 to +0.16. Lipsey & Wilson (1993) reported a difference of +0.53 (published) to +0.39 (unpublished) in a study of psychological, behavioral and educational interventions. Similar outcomes have been reported by Polanin, Tanner-Smith, & Hennessy (2016), and many others. Based on these long-established findings, Lipsey & Wilson (1993) suggested that meta-analyses should establish clear, rigorous criteria for study inclusion, but should then include every study that meets those standards, published or not.

The rationale for restricting interest (or meta-analyses) to published articles was always weak, but in recent years it is diminishing. An increasing proportion of the gray literature consists of technical reports, usually by third-party evaluators, of highly funded experiments. For example, experiments funded by IES and i3 in the U.S., the Education Endowment Foundation (EEF) in the U.K., and the World Bank and other funders in developing countries, provide sufficient resources to do thorough, high-quality implementations of experimental treatments, as well as state-of-the-art evaluations. These evaluations almost always meet the standards of the What Works Clearinghouse, Evidence for ESSA, and other review facilities, but they are rarely published, especially because third-party evaluators have little incentive to publish.

It is important to note that the number of high-quality unpublished studies is very large. Among the 645 studies reviewed by Cheung & Slavin (2016), all had to meet rigorous standards. Across all of them, 383 (59%) were unpublished. Excluding such studies would greatly diminish the number of high-quality experiments in any review.

I have the greatest respect for articles published in top refereed journals. Journal articles provide much that tech reports rarely do, such as extensive reviews of the literature, context for the study, and discussions of theory and policy. However, the fact that an experimental study appeared in a top journal does not indicate that the article’s findings are representative of all the research on the topic at hand.

The upshot of this discussion is clear. First, meta-analyses of experimental studies should always establish methodological criteria for inclusion (e.g., use of control groups, measures not overaligned or made by developers or researchers, duration, sample size), but never restrict studies to those that appeared in published sources. Second, readers of reviews of research on experimental studies should ignore the findings of reviews that were limited to published articles.

In the popular press, it’s fine to celebrate Magic Johnson’s triumphs and ignore his bad days. But if you want to know his stats, you need to include all of his games, not just the great ones. So it is with research in education. Focusing only on published findings can make us believe in magic, when what we need are the facts.

 References

Atkinson, D. R., Furlong, M. J., & Wampold, B. E. (1982). Statistical significance, reviewer evaluations, and the scientific process: Is there a (statistically) significant relationship? Journal of Counseling Psychology, 29(2), 189–194. https://doi.org/10.1037/0022-0167.29.2.189

Cheung, A., & Slavin, R. (2016). How methodological features affect effect sizes in education. Educational Researcher, 45 (5), 283-292.

Glass, G. V., McGraw, B., & Smith, M. L. (1981). Meta-analysis in social research. Beverly Hills: Sage Publications.

Lipsey, M.W. & Wilson, D. B. (1993). The efficacy of psychological, educational, and behavioral treatment: Confirmation from meta-analysis. American Psychologist, 48, 1181-1209.

Polanin, J. R., Tanner-Smith, E. E., & Hennessy, E. A. (2016). Estimating the difference between published and unpublished effect sizes: A meta-review. Review of Educational Research, 86(1), 207–236. https://doi.org/10.3102/0034654315582067

 

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

 

On Reviews of Research in Education

Not so long ago, every middle class home had at least one encyclopedia. Encyclopedias were prominently displayed, a statement to all that this was a house that valued learning. People consulted the encyclopedia to find out about things of interest to them. Those who did not own encyclopedias found them in the local library, where they were heavily used. As a kid, I loved everything about encyclopedias. I loved to read them, but also loved their musty small, their weight, and their beautiful maps and photos.

There were two important advantages of an encyclopedia. First, it was encyclopedic, so users could be reasonably certain that whatever information they wanted was in there somewhere. Second, they were authoritative. Whatever it said in the encyclopedia was likely to be true, or at least carefully vetted by experts.

In educational research, and all scientific fields, we have our own kinds of encyclopedias. One consists of articles in journals that publish reviews of research. In our field, the Review of Educational Research plays a pre-eminent role in this, but there are many others. Reviews are hugely popular. Invariably, review journals have a much higher citation count than even the most esteemed journals focusing on empirical research. In addition to journals, reviews appear I edited volumes, in online compendia, in technical reports, and other sources. At Johns Hopkins, we produce a bi-weekly newsletter, Best Evidence in Brief (BEiB; https://beibindex.wordpress.com/) that summarizes recent research in education. Two years ago we looked at analytics to find out the favorite articles from BEiB. Although BEiB mostly summarizes individual studies, almost all of its favorite articles were summaries of the findings of recent reviews.

Over time, RER and other review journals become “encyclopedias” of a sort.  However, they are not encyclopedic. No journal tries to ensure that key topics will all be covered over time. Instead, journal reviewers and editors evaluate each review sent to them on its own merits. I’m not criticizing this, but it is the way the system works.

Are reviews in journals authoritative? They are in one sense, because reviews accepted for publication have been carefully evaluated by distinguished experts on the topic at hand. However, review methods vary widely and reviews are written for many purposes. Some are written primarily for theory development, and some are really just essays with citations. In contrast, one category of reviews, meta-analyses, go to great lengths to locate and systematically include all relevant citations. These are not pure types, and most meta-analyses have at least some focus on theory building and discussion of current policy or research issues, even if their main purpose is to systematically review a well-defined set of studies.

Given the state of the art of research reviews in education, how could we create an “encyclopedia” of evidence from all sources on the effectiveness of programs and practices designed to improve student outcomes? The goal of such an activity would be to provide readers with something both encyclopedic and authoritative.

My colleagues and I created two websites that are intended to serve as a sort of encyclopedia of PK-12 instructional programs. The Best Evidence Encyclopedia (BEE; www.bestevidence.org) consists of meta-analyses written by our staff and students, all of which use similar inclusion criteria and review methods. These are used by a wide variety of readers, especially but not only researchers. The BEE has meta-analyses on elementary and secondary reading, reading for struggling readers, writing programs, programs for English learners, elementary and secondary mathematics, elementary and secondary science, early childhood programs, and other topics, so at least as far as achievement outcomes are concerned, it is reasonably encyclopedic. Our second website is Evidence for ESSA, designed more for educators. It seeks to include every program currently in existence, and therefore is truly encyclopedic in reading and mathematics. Sections on social emotional learning, attendance, and science are in progress.

Are the BEE and Evidence for ESSA authoritative as well as encyclopedic? You’ll have to judge for yourself. One important indicator of authoritativeness for the BEE is that all of the meta-analyses are eventually published, so the reviewers for those journals could be considered to be lending authority.

The What Works Clearinghouse (https://ies.ed.gov/ncee/wwc/) could be considered authoritative, as it is a carefully monitored online publication of the U.S. Department of Education. But is it encyclopedic? Probably not, for two reasons. One is that the WWC has difficulty keeping up with new research. Secondly, the WWC does not list programs that do not have any studies that meet its standards. As a result of both of these, a reader who types in the name of a current program may find nothing at all on it. Is this because the program did not meet WWC standards, or because the WWC has not yet reviewed it? There is no way to tell. Still, the WWC makes important contributions in the areas it has reviewed.

Beyond the websites focused on achievement, the most encyclopedic and authoritative source is Blueprints (www.blueprintsprograms.org). Blueprints focuses on drug and alcohol abuse, violence, bullying, social emotional learning, and other topics not extensively covered in other review sources.

In order to provide readers with easy access to all of the reviews meeting a specified level of quality on a given topic, it would be useful to have a source that briefly describes various reviews, regardless of where they appear. For example, a reader might want to know about all of the meta-analyses that focus on elementary mathematics, or dropout prevention, or attendance. These would include review articles published in scientific journals, technical reports, websites, edited volumes, and so on. To be cited in detail, the reviews should have to meet agreed-upon criteria, including a restriction to experimental-control comparison, a broad and well-documented search for eligible studies, documented efforts to include all studies (published or unpublished) that fall within well-specified parameters (e.g., subjects, grade levels, and start and end dates of studies included). Reviews that meet these standards might be highlighted, though others, including less systematic reviews, should be listed as well, as supplementary resources.

Creating such a virtual encyclopedia would be a difficult but straightforward task. At the end, the collection of rigorous reviews would offer readers encyclopedic, authoritative information on the topics of their interest, as well as providing something more important that no paper encyclopedias ever included: contrasting viewpoints from well-informed experts on each topic.

My imagined encyclopedia wouldn’t have the hypnotic musty smell, the impressive heft, or the beautiful maps and photos of the old paper encyclopedias. However, it would give readers access to up-to-date, curated, authoritative, quantitative reviews of key topics in education, with readable and appealing summaries of what was concluded in qualifying reviews.

Also, did I mention that unlike the encyclopedias of old, it would have to be free?

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

“But It Worked in the Lab!” How Lab Research Misleads Educators

In researching John Hattie’s meta-meta analyses, and digging into the original studies, I discovered one underlying factor that more than anything explains why he consistently comes up with greatly inflated effect sizes:  Most studies in the meta-analyses that he synthesizes are brief, small, artificial lab studies. And lab studies produce very large effect sizes that have little if any relevance to classroom practice.

This discovery reminds me of one of the oldest science jokes in existence: (One scientist to another): “Your treatment worked very well in practice, but how will it work in the lab?” (Or “…in theory?”)

The point of the joke, of course, is to poke fun at scientists more interested in theory than in practical impacts on real problems. Personally, I have great respect for theory and lab studies. My very first publication as a psychology undergraduate involved an experiment on rats.

Now, however, I work in a rapidly growing field that applies scientific methods to the study and improvement of classroom practice.  In our field, theory also has an important role. But lab studies?  Not so much.

A lab study in education is, in my view, any experiment that tests a treatment so brief, so small, or so artificial that it could never be used all year. Also, an evaluation of any treatment that could never be replicated, such as a technology program in which a graduate student is standing by every four students every day of the experiment, or a tutoring program in which the study author or his or her students provide the tutoring, might be considered a lab study, even if it went on for several months.

Our field exists to try to find practical solutions to practical problems in an applied discipline.  Lab studies have little importance in this process, because they are designed to eliminate all factors other than the variables of interest. A one-hour study in which children are asked to do some task under very constrained circumstances may produce very interesting findings, but cannot recommend practices for real teachers in real classrooms.  Findings of lab studies may suggest practical treatments, but by themselves they never, ever validate practices for classroom use.

Lab studies are almost invariably doomed to success. Their conditions are carefully set up to support a given theory. Because they are small, brief, and highly controlled, they produce huge effect sizes. (Because they are relatively easy and inexpensive to do, it is also very easy to discard them if they do not work out, contributing to the universally reported tendency of studies appearing in published sources to report much higher effects than reports in unpublished sources).  Lab studies are so common not only because researchers believe in them, but also because they are easy and inexpensive to do, while meaningful field experiments are difficult and expensive.   Need a publication?  Randomly assign your college sophomores to two artificial treatments and set up an experiment that cannot fail to show significant differences.  Need a dissertation topic?  Do the same in your third-grade class, or in your friend’s tenth grade English class.  Working with some undergraduates, we once did three lab studies in a single day. All were published. As with my own sophomore rat study, lab experiments are a good opportunity to learn to do research.  But that does not make them relevant to practice, even if they happen to take place in a school building.

By doing meta-analyses, or meta-meta-analyses, Hattie and others who do similar reviews obscure the fact that many and usually most of the studies they include are very brief, very small, and very artificial, and therefore produce very inflated effect sizes.  They do this by covering over the relevant information with numbers and statistics rather than information on individual studies, and by including such large numbers of studies that no one wants to dig deeper into them.  In Hattie’s case, he claims that Visible Learning meta-meta-analyses contain 52,637 individual studies.  Who wants to read 52,637 individual studies, only to find out that most are lab studies and have no direct bearing on classroom practice?  It is difficult for readers to do anything but assume that the 52,637 studies must have taken place in real classrooms, and achieved real outcomes over meaningful periods of time.  But in fact, the few that did this are overwhelmed by the thousands of lab studies that did not.

Educators have a right to data that are meaningful for the practice of education.  Anyone who recommends practices or programs for educators to use needs to be open about where that evidence comes from, so educators can judge for themselves whether or not one-hour or one-week studies under artificial conditions tell them anything about how they should teach. I think the question answers itself.

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

John Hattie is Wrong

John Hattie is a professor at the University of Melbourne, Australia. He is famous for a book, Visible Learning, which claims to review every area of research that relates to teaching and learning. He uses a method called “meta-meta-analysis,” averaging effect sizes from many meta-analyses. The book ranks factors from one to 138 in terms of their effect sizes on achievement measures. Hattie is a great speaker, and many educators love the clarity and simplicity of his approach. How wonderful to have every known variable reviewed and ranked!

However, operating on the principle that anything that looks to be too good to be true probably is, I looked into Visible Learning to try to understand why it reports such large effect sizes. My colleague, Marta Pellegrini from the University of Florence (Italy), helped me track down the evidence behind Hattie’s claims. And sure enough, Hattie is profoundly wrong. He is merely shoveling meta-analyses containing massive bias into meta-meta-analyses that reflect the same biases.

Part of Hattie’s appeal to educators is that his conclusions are so easy to understand. He even uses a system of dials with color-coded “zones,” where effect sizes of 0.00 to +0.15 are designated “developmental effects,” +0.15 to +0.40 “teacher effects” (i.e., what teachers can do without any special practices or programs), and +0.40 to +1.20 the “zone of desired effects.” Hattie makes a big deal of the magical effect size +0.40, the “hinge point,” recommending that educators essentially ignore factors or programs below that point, because they are no better than what teachers produce each year, from fall to spring, on their own. In Hattie’s view, an effect size of from +0.15 to +0.40 is just the effect that “any teacher” could produce, in comparison to students not being in school at all. He says, “When teachers claim that they are having a positive effect on achievement or when a policy improves achievement, this is almost always a trivial claim: Virtually everything works. One only needs a pulse and we can improve achievement.” (Hattie, 2009, p. 16). An effect size of 0.00 to +0.15 is, he estimates, “what students could probably achieve if there were no schooling” (Hattie, 2009, p. 20). Yet this characterization of dials and zones misses the essential meaning of effect sizes, which are rarely used to measure the amount teachers’ students gain from fall to spring, but rather the amount students receiving a given treatment gained in comparison to gains made by similar students in a control group over the same period. So an effect size of, say, +0.15 or +0.25 could be very important.

Hattie’s core claims are these:

• Almost everything works
• Any effect size less than +0.40 is ignorable
• It is possible to meaningfully rank educational factors in comparison to each other by averaging the findings of meta-analyses.

These claims appear appealing, simple, and understandable. But they are also wrong.

The essential problem with Hattie’s meta-meta-analyses is that they accept the results of the underlying meta-analyses without question. Yet many, perhaps most meta-analyses accept all sorts of individual studies of widely varying standards of quality. In Visible Learning, Hattie considers and then discards the possibility that there is anything wrong with individual meta-analyses, specifically rejecting the idea that the methods used in individual studies can greatly bias the findings.

To be fair, a great deal has been learned about the degree to which particular study characteristics bias study findings, always in a positive (i.e., inflated) direction. For example, there is now overwhelming evidence that effect sizes are significantly inflated in studies with small sample sizes, brief durations, use measures made by researchers or developers, are published (vs. unpublished), or use quasi-experiments (vs. randomized experiments) (Cheung & Slavin, 2016). Many meta-analyses even include pre-post studies, or studies that do not have pretests, or have pretest differences but fail to control for them. For example, I once criticized a meta-analysis of gifted education in which some studies compared students accepted into gifted programs to students rejected for those programs, controlling for nothing!

A huge problem with meta-meta-analysis is that until recently, meta-analysts rarely screened individual studies to remove those with fatal methodological flaws. Hattie himself rejects this procedure: “There is…no reason to throw out studies automatically because of lower quality” (Hattie, 2009, p. 11).

In order to understand what is going on in the underlying meta-analyses in a meta-meta-analysis, is it crucial to look all the way down to the individual studies. As a point of illustration, I examined Hattie’s own meta-meta-analysis of feedback, his third ranked factor, with a mean effect size of +0.79. Hattie & Timperly (2007) located 12 meta-analyses. I found some of the ones with the highest mean effect sizes.

At a mean of +1.24, the meta-analysis with the largest effect size in the Hattie & Timperley (2007) review was a review of research on various reinforcement treatments for students in special education by Skiba, Casey, & Center (1985-86). The reviewers required use of single-subject designs, so the review consisted of a total of 35 students treated one at a time, across 25 studies. Yet it is known that single-subject designs produce much larger effect sizes than ordinary group designs (see What Works Clearinghouse, 2017).

The second-highest effect size, +1.13, was from a meta-analysis by Lysakowski & Walberg (1982), on instructional cues, participation, and corrective feedback. Not enough information is provided to understand the individual studies, but there is one interesting note. A study using a single-subject design, involving two students, had an effect size of 11.81. That is the equivalent of raising a child’s IQ from 100 to 277! It was “winsorized” to the next-highest value of 4.99 (which is like adding 75 IQ points). Many of the studies were correlational, with no controls for inputs, or had no control group, or were pre-post designs.

A meta-analysis by Rummel and Feinberg (1988), with a reported effect size of +0.60, is perhaps the most humorous inclusion in the Hattie & Timperley (2007) meta-meta-analysis. It consists entirely of brief lab studies of the degree to which being paid or otherwise reinforced for engaging in an activity that was already intrinsically motivating would reduce subjects’ later participation in that activity. Rummel & Feinberg (1988) reported a positive effect size if subjects later did less of the activity they were paid to do. The reviewers decided to code studies positively if their findings corresponded to the theory (i.e., that feedback and reinforcement reduce later participation in previously favored activities), but in fact their “positive” effect size of +0.60 indicates a negative effect of feedback on performance.

I could go on (and on), but I think you get the point. Hattie’s meta-meta-analyses grab big numbers from meta-analyses of all kinds with little regard to the meaning or quality of the original studies, or of the meta-analyses.

If you are familiar with the What Works Clearinghouse (2007), or our own Best-Evidence Syntheses (www.bestevidence.org) or Evidence for ESSA (www.evidenceforessa.org), you will know that individual studies, except for studies of one-to-one tutoring, almost never have effect sizes as large as +0.40, Hattie’s “hinge point.” This is because WWC, BEE, and Evidence for ESSA all very carefully screen individual studies. We require control groups, controls for pretests, minimum sample sizes and durations, and measures independent of the treatments. Hattie applies no such standards, and in fact proclaims that they are not necessary.

It is possible, in fact essential, to make genuine progress using high-quality rigorous research to inform educational decisions. But first we must agree on what standards to apply.  Modest effect sizes from studies of practical treatments in real classrooms over meaningful periods of time on measures independent of the treatments tell us how much a replicable treatment will actually improve student achievement, in comparison to what would have been achieved otherwise. I would much rather use a program with an effect size of +0.15 from such studies than to use programs or practices found in studies with major flaws to have effect sizes of +0.79. If they understand the situation, I’m sure all educators would agree with me.

To create information that is fair and meaningful, meta-analysts cannot include studies of unknown and mostly low quality. Instead, they need to apply consistent standards of quality for each study, to look carefully at each one and judge its freedom from bias and major methodological flaws, as well as its relevance to practice. A meta-analysis cannot be any better than the studies that go into it. Hattie’s claims are deeply misleading because they are based on meta-analyses that themselves accepted studies of all levels of quality.

Evidence matters in education, now more than ever. Yet Hattie and others who uncritically accept all studies, good and bad, are undermining the value of evidence. This needs to stop if we are to make solid progress in educational practice and policy.

References

Cheung, A., & Slavin, R. (2016). How methodological features affect effect sizes in education. Educational Researcher, 45 (5), 283-292.

Hattie, J. (2009). Visible learning. New York, NY: Routledge.

Hattie, J., & Timperley, H. (2007). The power of feedback. Review of Educational Research, 77 (1), 81-112.

Lysakowski, R., & Walberg, H. (1982). Instructional effects of cues, participation, and corrective feedback: A quantitative synthesis. American Educational Research Journal, 19 (4), 559-578.

Rummel, A., & Feinberg, R. (1988). Cognitive evaluation theory: A review of the literature. Social Behavior and Personality, 16 (2), 147-164.

Skiba, R., Casey, A., & Center, B. (1985-86). Nonaversive procedures I the treatment of classroom behavior problems. The Journal of Special Education, 19 (4), 459-481.

What Works Clearinghouse (2017). Procedures handbook 4.0. Washington, DC: Author.

Photo credit: U.S. Farm Security Administration [Public domain], via Wikimedia Commons

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

 

Meta-Analysis and Its Discontents

Everyone loves meta-analyses. We did an analysis of the most frequently opened articles on Best Evidence in Brief. Almost all of the most popular were meta-analyses. What’s so great about meta-analyses is that they condense a lot of evidence and synthesize it, so instead of just one study that might be atypical or incorrect, a meta-analysis seems authoritative, because it averages many individual studies to find the true effect of a given treatment or variable.

Meta-analyses can be wonderful summaries of useful information. But today I wanted to discuss how they can be misleading. Very misleading.

The problem is that there are no norms among journal editors or meta-analysts themselves about standards for including studies or, perhaps most importantly, how much or what kind of information needs to be reported about each individual study in a meta-analysis. Some meta-analyses are completely statistical. They report all sorts of statistics and very detailed information on exactly how the search for articles took place, but never say anything about even a single study. This is a problem for many reasons. Readers may have no real understanding of what the studies really say. Even if citations for the included studies are available, only a very motivated reader is going to go find any of them. Most meta-analyses do have a table listing studies, but the information in the table may be idiosyncratic or limited.

One reason all of this matters is that without clear information on each study, readers can be easily misled. I remember encountering this when meta-analysis first became popular in the 1980s. Gene Glass, who coined the very term, proposed some foundational procedures, and popularized the methods. Early on, he applied meta-analysis to determine the effects of class size, which by then had been studied several times and found to matter very little except in first grade. Reducing “class size” to one (i.e., one-to-one tutoring) also was known to make a big difference, but few people would include one-to-one tutoring in a review of class size. But Glass and Smith (1978) found a much higher effect, not limited to first grade or tutoring. It was a big deal at the time.

I wanted to understand what happened. I bought and read Glass’ book on class size, but it was nearly impossible to tell what had happened. But then I found in an obscure appendix a distribution of effect sizes. Most studies had effect sizes near zero, as I expected. But one had a huge effect size, of +1.25! It was hard to tell which particular study accounted for this amazing effect but I searched by process of elimination and finally found it.

It was a study of tennis.

The outcome measure was the ability to “rally a ball against a wall so many times in 30 seconds.” Not surprisingly, when there were “large class sizes,” most students got very few chances to practice, while in “small class sizes,” they did.

If you removed the clearly irrelevant tennis study, the average effect size for class sizes (other than tutoring) dropped to near zero, as reported in all other reviews (Slavin, 1989).

The problem went way beyond class size, of course. What was important, to me at least, was that Glass’ presentation of the data made it very difficult to find out what was really going on. He had attractive and compelling graphs and charts showing effects of class size, but they all depended on the one tennis study, and there was no easy way to find out.

Because of this review and several others appearing in the 1980s, I wrote an article criticizing numbers–only meta-analyses and arguing that reviewers should show all of the relevant information about the studies in their meta-analyses, and should even describe each study briefly to help readers understand what was happening. I made up a name for this, “best-evidence synthesis” (Slavin, 1986).

Neither the term nor the concept really took hold, I’m sad to say. You still see meta-analyses all the time that do not tell readers enough for them to know what’s really going on. Yet several developments have made the argument for something like best-evidence synthesis a lot more compelling.

One development is the increasing evidence that methodological features can be strongly correlated with effect sizes (Cheung & Slavin, 2016). The evidence is now overwhelming that effect sizes are greatly inflated when sample sizes are small, when study durations are brief, when measures are made by developers or researchers, or when quasi-experiments rather than randomized experiments are used, for example. Many meta-analyses check for the effects of these and other study characteristics, and may make adjustments if there are significant differences. But this is not sufficient, because in a particular meta-analysis, there may not be enough studies to make any study-level factors significant. For example, if Glass had tested “tennis vs. non-tennis,” there would have been no significant difference, because there was only one tennis study. Yet that one study dominated the means anyway. Eliminating studies using, for example, researcher/developer-made measures or very small sample sizes or very brief durations is one way to remove bias from meta-analyses, and this is what we do in our reviews. But at bare minimum, it is important to have enough information available in tables to enable readers or journal reviewers to look for such biasing factors so they can recompute or at least understand the main effects if they are so inclined.

The second development that makes it important to require more information on individual studies in meta-analyses is the increased popularity of meta-meta-analyses, where the average effect sizes from whole meta-analyses are averaged. These have even more potential for trouble than the worst statistics-only reviews, because it is extremely unlikely that many readers will follow the citations to each included meta-analysis and then follow those citations to look for individual studies. It would be awfully helpful if readers or reviewers could trust the individual meta-analyses (and therefore their averages), or at least see for themselves.

As evidence takes on greater importance, this would be a good time to discuss reasonable standards for meta-analyses. Otherwise, we’ll be rallying balls uselessly against walls forever.

References

Cheung, A., & Slavin, R. (2016). How methodological features affect effect sizes in education. Educational Researcher, 45 (5), 283-292

Glass, G., & Smith, M. L. (1978). Meta-Analysis of research on the relationship of class size and achievement. San Francisco: Far West Laboratory for Educational Research and Development.

Slavin, R.E. (1986). Best-evidence synthesis: An alternative to meta-analytic and traditional reviews. Educational Researcher, 15 (9), 5-11.

Slavin, R. E. (1989). Class size and student achievement:  Small effects of small classes. Educational Psychologist, 24, 99-110.

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

Effect Sizes and the 10-Foot Man

If you ever go into the Ripley’s Believe It or Not Museum in Baltimore, you will be greeted at the entrance by a statue of the tallest man who ever lived, Robert Pershing Wadlow, a gentle giant at 8 feet, 11 inches in his stocking feet. Kids and adults love to get their pictures taken standing by him, to provide a bit of perspective.

I bring up Mr. Wadlow to explain a phrase I use whenever my colleagues come up with an effect size of more than 1.00. “That’s a 10-foot man,” I say. What I mean, of course, is that while it is not impossible that there could be a 10-foot man someday, it is extremely unlikely, because there has never been a man that tall in all of history. If someone reports seeing one, they are probably mistaken.

In the case of effect sizes you will never, or almost never, see an effect size of more than +1.00, assuming the following reasonable conditions:

1. The effect size compares experimental and control groups (i.e., it is not pre-post).
2. The experimental and control group started at the same level, or they started at similar levels and researchers statistically controlled for pretest differences.
3. The measures involved were independent of the researcher and the treatment, not made by the developers or researchers. The test was not given by the teachers to their own students.
4. The treatment was provided by ordinary teachers, not by researchers, and could in principle be replicated widely in ordinary schools. The experiment had a duration of at least 12 weeks.
5. There were at least 30 students and 2 teachers in each treatment group (experimental and control).

If these conditions are met, the chances of finding effect sizes of more than +1.00 are about the same as the chances of finding a 10-foot man. That is, zero.

I was thinking about the 10-foot man when I was recently asked by a reporter about the “two sigma effect” claimed by Benjamin Bloom and much discussed in the 1970s and 1980s. Bloom’s students did a series of experiments in which students were taught about a topic none of them knew anything about, usually principles of sailing. After a short period, students were tested. Those who did not achieve at least 80% (defined as “mastery”) on the tests were tutored by University of Chicago graduate students long enough to ensure that every tutored student reached mastery. The purpose of this demonstration was to make a claim that every student could learn whatever we wanted to teach them, and the only variable was instructional time, as some students need more time to learn than others. In a system in which enough time could be given to all, “ability” would disappear as a factor in outcomes. Also, in comparison to control groups who were not taught about sailing at all, the effect size was often more than 2.0, or two sigma. That’s why this principle was called the “two sigma effect.” Doesn’t the two sigma effect violate my 10-foot man principle?

No, it does not. The two sigma studies used experimenter-made tests of content taught to the experimental but not control groups. It used University of Chicago graduate students providing far more tutoring (as a percentage of initial instruction) than any school could ever provide. The studies were very brief and sample sizes were small. The two sigma experiments were designed to prove a point, not to evaluate a feasible educational method.

A more recent example of the 10-foot man principle is found in Visible Learning, the currently fashionable book by John Hattie claiming huge effect sizes for all sorts of educational treatments. Hattie asks the reader to ignore any educational treatment with an effect size of less than +0.40, and reports many whole categories of teaching methods with average effect sizes of more than +1.00. How can this be?

The answer is that such effect sizes, like two sigma, do not incorporate the conditions I laid out. Instead, Hattie throws into his reviews entire meta-analyses which may include pre-post studies, studies using researcher-made measures, studies with tiny samples, and so on. For practicing educators, such effect sizes are useless. An educator knows that all children grow from pre- to posttest. They would not (and should not) accept measures made by researchers. The largest known effect sizes that do meet the above conditions are one-to-one tutoring studies with effect sizes up to +0.86. Still not +1.00. What could be more effective than the best of 1-1 tutoring?

It’s fun to visit Mr. Wadlow at the museum, and to imagine what an ever taller man could do on a basketball team, for example. But if you see a 10-foot man at Ripley’s Believe it or Not, or anywhere else, here’s my suggestion. Don’t believe it. And if you visit a museum of famous effect sizes that displays a whopper effect size of +1.00, don’t believe that, either. It doesn’t matter how big effect sizes are if they are not valid.

A 10-foot man would be a curiosity. An effect size of +1.00 is a distraction. Our work on evidence is too important to spend our time looking for 10-foot men, or effect sizes of +1.00, that don’t exist.

Photo credit: [Public domain], via Wikimedia Commons

This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.

On Meta-Analysis: Eight Great Tomatoes

I remember a long-ago advertisement for Contadina tomato paste. It went something like this:

Eight great tomatoes in an itsy bitsy can!

This ad creates an appealing image, or at least a provocative one, that I suppose sold a lot of tomato paste.

In educational research, we do something a lot like “eight great tomatoes.” It’s called meta-analysis, or systematic review.  I am particularly interested in meta-analyses of experimental studies of educational programs.  For example, there are meta-analyses of reading and math and science programs.  I’ve written them myself, as have many others.  In each, some number of relevant studies are identified.  From each study, one or more “effect sizes” are computed to represent the impact of the program on important outcomes, such as scores on achievement tests. These are then averaged to get an overall impact for each program or type of program.  Think of the effect size as boiling down tomatoes to make concentrated paste, to fit into an itsy bitsy can.

But here is the problem.  The Contadina ad specifies eight great tomatoes. If even one tomato is instead a really lousy one, the contents of the itsy bitsy can will be lousy.  Ultimately, lousy tomato pastes would bankrupt the company.

The same is true of meta-analyses.  Some meta-analyses include a broad range of studies – good, mediocre, and bad.  They may try to statistically control for various factors, but this does not do the job.  Bad studies lead to bad outcomes.  Years ago, I critiqued a study of “class size.”  The studies of class size in ordinary classrooms found small effects.  But there was one study that involved teaching tennis.  In small classes, the kids got a lot more court time than did kids in large classes.  This study, and only this study, found substantial effects of class size, significantly affecting the average.  There were not eight great tomatoes, there was at least one lousy tomato, which made the itsy bitsy can worthless.

The point I am making here is that when doing meta-analysis, the studies must be pre-screened for quality, and then carefully scrubbed.  Specifically, there are many factors that greatly (and falsely) inflate effect size.  Examples include use of assessments made by the researchers and ones that assess what was taught in the experimental group but not the control group, use of small samples, and provision of excessive assistance to the teachers.

Some meta-analyses just shovel all the studies onto a computer and report an average effect size.  More responsible ones shovel the studies into a computer and then test for and control for various factors that might affect outcomes. This is better, but you just can’t control for lousy studies, because they are often lousy in many ways.

Instead, high-quality meta-analyses set specific criteria for inclusion intended to minimize bias.  Studies often use both valid measures and crummy measures (such as those biased toward the experimental group).  Good meta-analyses use the good measures but not the (defined in advance) crummy ones.  Studies that only used crummy measures are excluded.  And so on.

With systematic standards, systematically applied, meta-analyses can be of great value.  Call it the Contadina method.  In order to get great tomato paste, start with great tomatoes. The rest takes care of itself.