“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?”)

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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.

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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.

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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.

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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.

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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.