blog posts and news stories

View from the West Coast: Relevance is More Important than Methodological Purity

Bob Slavin published a blog post in which he argues that evaluation research can be damaged by using the cloud-based data routinely collected by today’s education technology (edtech). We see serious flaws with this argument and it is quite clear that he directly opposes the position we have taken in a number of papers and postings, and also discussed as part of the west coast conversations about education research policy. Namely, we’ve argued that using the usage data routinely collected by edtech can greatly improve the relevance and usefulness of evaluations.

Bob’s argument is that if you use data collected during the implementation of the program to identify students and teachers who used the product as intended, you introduce bias. The case he is concerned with is in a matched comparison study (or quasi-experiment) where the researcher has to find the right matching students or classes to the students using the edtech. The key point he makes is:

“students who used the computers [or edtech product being evaluated] were more motivated or skilled than other students in ways the pretests do not detect.”

That is, there is an unmeasured characteristic, let’s call it motivation, that both explains the student’s desire to use the product and explains why they did better on the outcome measure. Since the characteristic is not measured, you don’t know which students in the control classes have this motivation. If you select the matching students only on the basis of their having the same pretest level, demographics, and other measured characteristics but you don’t match on “motivation”, you have biased the result.

The first thing to note about this concern, is that there may not be a factor such motivation that explains both edtech usage and the favorable outcome. It is just that there is a theoretical possibility that such a variable is driving the result. The bias may or may not be there and to reject a method because there is an unverifiable possibility of bias is an extreme move.

Second, it is interesting that he uses an example that seems concrete but is not at all specific to the bias mechanism he’s worried about.

“Sometimes teachers use computer access as a reward for good work, or as an extension activity, in which case the bias is obvious.”

This isn’t a problem of an unmeasured variable at all. The problem is that the usage didn’t cause the improvement—rather, the improvement caused the usage. This would be a problem in a randomized “gold standard” experiment. The example makes it sound like the problem is “obvious” and concrete, when Bob’s concern is purely theoretical. This example is a good argument for having the kind of implementation analyses of the sort that ISTE is doing in their Edtech Advisor and Jefferson Education Exchange has embarked on.

What is most disturbing about Bob’s blog post is that he makes a statement that is not supported by the ESSA definitions or U.S. Department of Education regulations or guidance. He claims that:

“In order to reach the second level (“moderate”) of ESSA or Evidence for ESSA, a matched study must do everything a randomized study does, including emphasizing ITT [Intent To Treat, i.e., using all students in the pre-identified schools or classes where administrators intended to use the product] estimates, with the exception of randomizing at the start.”

It is true that Bob’s own site Evidence for ESSA, will not accept any study that does not follow the ITT protocol but ESSA, itself, does not require that constraint.

Essentially, Bob is throwing away relevance to school decision-makers in order to maintain an unnecessary purity of research design. School decision-makers care whether the product is likely to work with their school’s population and available resources. Can it solve their problem (e.g., reduce achievement gaps among demographic categories) if they can implement it adequately? Disallowing efficacy studies that consider compliance to a pre-specified level of usage in selecting the “treatment group” is to throw out relevance in favor or methodological purity. Yes, there is a potential for bias, which is why ESSA considers matched-comparison efficacy studies to be “moderate” evidence. But school decisions aren’t made on the basis of which product has the largest average effect when all the non-users are included. A measure of subgroup differences, when the implementation is adequate, provides more useful information.

The Rebel Alliance is Growing

The rebellion against the old NCLB way of doing efficacy research is gaining force. A growing community among edtech developers, funders, researchers, and school users has been meeting in an attempt to reach a consensus on an alternative built on ESSA.

This is being assisted by openness in the directions currently being pursued by IES. In fact, we are moving into a new phase marked by two-way communication with the regime. While the rebellion hasn’t yet handed over its lightsabers, it is encouraged by the level of interest from prominent researchers.

From these ongoing discussions, there have been some radical suggestions inching toward consensus. A basic idea now being questioned is this:

The difference between the average of the treatment group and the average of the control group is a valid measure of effectiveness.

There are two problems with this:

1. In schools, there’s no “placebo” or something that looks like a useful program but is known to have zero effectiveness. Whatever is going on in the schools, or classes, or with teachers and students in the control condition has some usefulness or effectiveness. The usefulness of the activities in the control classes or schools may be greater than the activities being evaluated in the study, or may be not as useful. The study may find that the “effectiveness” of the activities being studied is positive, negative, or too small to be discerned statistically by the study. In any case, the size (negative or positive) of the effect is determined as much by what’s being done in the control group as the treatment group.
2. Few educational activities have the same level of usefulness for all teachers and students. Looking at only the average will obscure the differences. For example, we ran a very large study for the U.S. Department of Education of a STEM program where we found, on average, the program was effective. What the department didn’t report was that it only worked for the white kids, not the black kids. The program increased instead of reducing the existing achievement gap. If you are considering adopting this STEM program, the impact on the different subgroups is relevant–a high minority school district may want to avoid it. Also, to make the program better, the developers need to know where it works and where it doesn’t. Again, the average impact is not just meaningless but also can be misleading.

A solution to the overuse of the average difference from studies is to conduct a lot more studies. The price the ED paid for our large study could have paid for 30 studies of the kind we are now conducting in the same state of the same program; in 10% of the time of the original study. If we had 10 different studies for each program, where studies are conducted in different school districts with different populations and levels of resources, the “average” across these studies start to make sense. Importantly, the average across these 10 studies for each of the subgroups will give a valid picture of where, how, and with which students and teachers the program tends to work best. This kind of averaging used in research is called meta-analysis and allows many small differences found across studies to build on the power of each study to generate reliable findings.

If developers or publishers of the products being used in schools took advantage of their hundreds of implementations to gather data, and if schools would be prepared to share student data for this research, we could have researcher findings that both help schools decide what will likely work for them and help developers improve their products.

A Rebellion Against the Current Research Regime

Finally! There is a movement to make education research more relevant to educators and edtech providers alike.

At various conferences, we’ve been hearing about a rebellion against the “business as usual” of research, which fails to answer the question of, “Will this product work in this particular school or community?” For educators, the motive is to find edtech products that best serve their students’ unique needs. For edtech vendors, it’s an issue of whether research can be cost-effective, while still identifying a product’s impact, as well as helping to maximize product/market fit.

The “business as usual” approach against which folks are rebelling is that of the U.S. Education Department (ED). We’ll call it the regime. As established by the Education Sciences Reform Act of 2002 and the Institute of Education Sciences (IES), the regime anointed the randomized control trial (or RCT) as the gold standard for demonstrating that a product, program, or policy caused an outcome.

Let us illustrate two ways in which the regime fails edtech stakeholders.

First, the regime is concerned with the purity of the research design, but not whether a product is a good fit for a school given its population, resources, etc. For example, in an 80-school RCT that the Empirical team conducted under an IES contract on a statewide STEM program, we were required to report the average effect, which showed a small but significant improvement in math scores (Newman et al., 2012). The table on page 104 of the report shows that while the program improved math scores on average across all students, it didn’t improve math scores for minority students. The graph that we provide here illustrates the numbers from the table and was presented later at a research conference.

IES had reasons couched in experimental design for downplaying anything but the primary, average finding, however this ignores the needs of educators with large minority student populations, as well as of edtech vendors that wish to better serve minority communities.

Our RCT was also expensive and took many years, which illustrates the second failing of the regime: conventional research is too slow for the fast-moving innovative edtech development cycles, as well as too expensive to conduct enough research to address the thousands of products out there.

These issues of irrelevance and impracticality were highlighted last year in an “academic symposium” of 275 researchers, edtech innovators, funders, and others convened by the organization now called Jefferson Education Exchange (JEX). A popular rallying cry coming out of the symposium is to eschew the regime’s brand of research and begin collecting product reviews from front-line educators. This would become a Consumer Reports for edtech. Factors associated with differences in implementation are cited as a major target for data collection. Bart Epstein, JEX’s CEO, points out: “Variability among and between school cultures, priorities, preferences, professional development, and technical factors tend to affect the outcomes associated with education technology. A district leader once put it to me this way: ‘a bad intervention implemented well can produce far better outcomes than a good intervention implemented poorly’.”

Here’s why the Consumer Reports idea won’t work. Good implementation of a program can translate into gains on outcomes of interest, such as improved achievement, reduction in discipline referrals, and retention of staff, but only if the program is effective. Evidence that the product caused a gain on the outcome of interest is needed or else all you measure is the ease of implementation and student engagement. You wouldn’t know if the teachers and students were wasting their time with a product that doesn’t work.

We at Empirical Education are joining the rebellion. The guidelines for research on edtech products we recently prepared for the industry and made available here is a step toward showing an alternative to the regime while adopting important advances in the Every Student Succeeds Act (ESSA).

We share the basic concern that established ways of conducting research do not answer the basic question that educators and edtech providers have: “Is this product likely to work in this school?” But we have a different way of understanding the problem. From years of working on federal contracts (often as a small business subcontractor), we understand that ED cannot afford to oversee a large number of small contracts. When there is a policy or program to evaluate, they find it necessary to put out multi-million-dollar, multi-year contracts. These large contracts suit university researchers, who are not in a rush, and large research companies that have adjusted their overhead rates and staffing to perform on these contracts. As a consequence, the regime becomes focused on the perfection in the design, conduct, and reporting of the single study that is intended to give the product, program, or policy a thumbs-up or thumbs-down.

There’s still a need for a causal research design that can link conditions such as resources, demographics, or teacher effectiveness with educational outcomes of interest. In research terminology, these conditions are called “moderators,” and in most causal study designs, their impact can be measured.

The rebellion should be driving an increase the number of studies by lowering their cost and turn-around time. Given our recent experience with studies of edtech products, this reduction can reach a factor of 100. Instead of one study that costs $3 million and takes 5 years, think in terms of a hundred studies that cost $30,000 each and are completed in less than a month. If for each product, there are 5 to 10 studies that are combined, they would provide enough variation and numbers of students and schools to detect differences in kinds of schools, kinds of students, and patterns of implementation so as to find where it works best. As each new study is added, our understanding of how it works and with whom improves.

It won’t be enough to have reviews of product implementation. We need an independent measure of whether—when implemented well—the intervention is capable of a positive outcome. We need to know that it can make (i.e., cause) a difference AND under what conditions. We don’t want to throw out research designs that can detect and measure effect sizes, but we should stop paying for studies that are slow and expensive.

Our guidelines for edtech research detail multiple ways that edtech providers can adapt research to better work for them, especially in the era of ESSA. Many of the key recommendations are consistent with the goals of the rebellion:

• The usage data collected by edtech products from students and teachers gives researchers very precise information on how well the program was implemented in each school and class. It identifies the schools and classes where implementation met the threshold for which the product was designed. This is a key to lowering cost and turn-around time.
• ESSA offers four levels of evidence which form a developmental sequence, where the base level is based on existing learning science and provides a rationale for why a school should try it. The next level looks for a correlation between an important element in the rationale (measured through usage of that part of the product) and a relevant outcome. This is accepted by ESSA as evidence of promise, informs the developers how the product works, and helps product marketing teams get the right fit to the market.
• The ESSA level that provides moderate evidence that the product caused the observed impact requires a comparison group matched to the students or schools that were identified as the users. The regime requires researchers to report only the difference between the user and comparison groups on average. Our guidelines insist that researchers must also estimate the extent to which an intervention is differentially effective for different demographic categories or implementation conditions.

From the point of view of the regime, nothing in these guidelines actually breaks the rules and regulations of ESSA’s evidence standards. Educators, developers, and researchers should feel empowered to collect data on implementation, calculate subgroup impacts, and use their own data to generate evidence sufficient for their own decisions.

A version of this article was published in the Edmarket Essentials magazine.

APPAM doesn’t stand for A Pretty Pithy Abbreviated Meeting

APPAM does stand for excellence, critical thinking, and quality research.

The 2017 fall research conference kept reminding me of one recurrent theme: bridging the chasms between researchers, policymakers, and practitioners.

Linear processes don’t work. Participatory research is critical!

Another hot topic is generalizability! There is a lot of work to be done here. What works? For whom? Why?

Lots of food for thought!

Understanding Logic Models Workshop Series

On July 17, Empirical Education facilitated the first of two workshops for practitioners in New Mexico on the development of program logic models, one of the first steps in developing a research agenda. The workshop, entitled “Identifying Essential Logic Model Components, Definitions, and Formats”, introduced the general concepts, purposes, and uses of program logic models to members of the Regional Education Lab (REL) Southwest’s New Mexico Achievement Gap Research Alliance. Throughout the workshop, participants collaborated with facilitators to build a logic model for a program or policy that participants are working on or that is of interest.

Empirical Education is part of the REL Southwest team, which assists Arkansas, Louisiana, New Mexico, Oklahoma, and Texas in using data and research evidence to address high-priority regional needs, including charter school effectiveness, early childhood education, Hispanic achievement in STEM, rural school performance, and closing the achievement gap, through six research alliances. The logic model workshops aim to strengthen the technical capacity of New Mexico Achievement Gap Research Alliance members to understand and visually represent their programs’ theories of change, identify key program components and outcomes, and use logic models to develop research questions. Both workshops are being held in Albuquerque, New Mexico.

Importance is Important for Rules of Evidence Proposed for ED Grant Programs

The U.S. Department of Education recently proposed new rules for including serious evaluations as part of its grant programs. The approach is modeled on how evaluations are used in the Investing in Innovation (i3) program where the proposal must show there’s some evidence that the proposed innovation has a chance of working and scaling and must include an evaluation that will add to a growing body of evidence about the innovation. We like this approach because it treats previous research as a hypothesis that the innovation may work in the new context. And each new grant is an opportunity to try the innovation in a new context, with improved approaches that warrant another check on effectiveness. But the proposed rules definitely had some weaknesses that were pointed out in the public comments available online. We hope ED heeds these suggestions.

Mark Schneiderman representing the Software and Information Industry Association (SIIA) recommends that outcomes used in effectiveness studies should not be limited to achievement scores.

SIIA notes that grant program resources could appropriately address a range of purposes from instructional to administrative, from assessment to professional development, and from data warehousing to systems productivity. The measures could therefore include such outcomes as student test scores, teacher retention rates, changes in classroom practice or efficiency, availability and use of data or other student/teacher/school outcomes, and cost effectiveness and efficiency that can be observed and measured. Many of these outcome measures can also be viewed as intermediate outcomes—changes in practice that, as demonstrated by other research, are likely to affect other final outcomes.

He also points out that quality of implementation and the nature of the comparison group can be the deciding factors in whether or not a program is found to be effective.

SIIA notes that in education there is seldom a pure control condition such as can be achieved in a medical trial with a placebo or sugar pill. Evaluations of education products and services resemble comparative effectiveness trials in which a new medication is tested against a currently approved one to determine whether it is significantly better. The same product may therefore prove effective in one district that currently has a weak program but relatively less effective in another where a strong program is in place. As a result, significant effects can often be difficult to discern.

This point gets to the heart of the contextual issues in any experimental evaluation. Without understanding the local conditions of the experiment the size of the impact for any other context cannot be anticipated. Some experimentalists would argue that a massive multi-site trial would allow averaging across many contextual variations. But such “on average” results won’t necessarily help the decision-maker working in specific local conditions. Thus, taking previous results as a rough indication that an innovation is worth trying is the first step before conducting the grant-funded evaluation of a new variation of the innovation under new conditions.

Jon Baron, writing for the Coalition for Evidence Based Policy expresses a fundamental concern about what counts as evidence. Jon, who is a former Chair of the National Board for Education Sciences and has been a prominent advocate for basing policy on rigorous research, suggests that

“the definition of ‘strong evidence of effectiveness’ in §77.1 incorporate the Investing in Innovation Fund’s (i3) requirement for effects that are ‘substantial and important’ and not just statistically significant.”

He cites examples where researchers have reported statistically significant results, which were based on trivial outcomes or had impacts so small as to have no practical value. Including “substantial and important” as additional criteria also captures the SIIA’s point that it is not sufficient to consider the internal validity of the study—policy makers must consider whether the measure used is an important one or whether the treatment-control contrast allows for detecting a substantial impact.

Addressing the substance and importance of the results gets us appropriately into questions of external validity, and leads us to questions about subgroup impact, where, for example, an innovation has a positive impact “on average” and works well for high scoring students but provides no value for low scoring students. We would argue that a positive average impact is not the most important part of the picture if the end result is an increase in a policy-relevant achievement gap. Should ED be providing grants for innovations where there has been a substantial indication that a gap is worsened? Probably yes, but only if the proposed development is aimed at fixing the malfunctioning innovation and if the program evaluation can address this differential impact.

The Value of Looking at Local Results

The report we released today has an interesting history that shows the value of looking beyond the initial results of an experiment. Later this week, we are presenting a paper at AERA entitled “In School Settings, Are All RCTs Exploratory?” The findings we report from our experiment with an iPad application were part of the inspiration for this. If Riverside Unified had not looked at its own data, we would not, in the normal course of data analysis, have broken the results out by individual districts, and our conclusion would have been that there was no discernible impact of the app. We can cite many other cases where looking at subgroups leads us to conclusions different from the conclusion based on the result averaged across the whole sample. Our report on AMSTI is another case we will cite in our AERA paper.

We agree with the Institute of Education Sciences (IES) in taking a disciplined approach in requiring that researchers “call their shots” by naming the small number of outcomes considered most important in any experiment. All other questions are fine to look at but fall into the category of exploratory work. What we want to guard against, however, is the implication that answers to primary questions, which often are concerned with average impacts for the study sample as a whole, must apply to various subgroups within the sample, and therefore can be broadly generalized by practitioners, developers, and policy makers.

If we find an average impact but in exploratory analysis discover plausible, policy-relevant, and statistically strong differential effects for subgroups, then some doubt about completeness may be cast on the value of the confirmatory finding. We may not be certain of a moderator effect—for example—but once it comes to light, the value of the average impact can also be considered incomplete or misleading for practical purposes. If it is necessary to conduct an additional experiment to verify a differential subgroup impact, the same experiment may verify that the average impact is not what practitioners, developers, and policy makers should be concerned with.

In our paper at AERA, we are proposing that any result from a school-based experiment should be treated as provisional by practitioners, developers, and policy makers. The results of RCTs can be very useful, but the challenges of generalizability of the results from even the most stringently designed experiment mean that the results should be considered the basis for a hypothesis that the intervention may work under similar conditions. For a developer considering how to improve an intervention, the specific conditions under which it appeared to work or not work is the critical information to have. For a school system decision maker, the most useful pieces of information are insight into subpopulations that appear to benefit and conditions that are favorable for implementation. For those concerned with educational policy, it is often the case that conditions and interventions change and develop more rapidly than research studies can be conducted. Using available evidence may mean digging through studies that have confirmatory results in contexts similar or different from their own and examining exploratory analyses that provide useful hints as to the most productive steps to take next. The practitioner in this case is in a similar position to the researcher considering the design of the next experiment. The practitioner also has to come to a hypothesis about how things work as the basis for action.

Exploration in the World of Experimental Evaluation

Our 300+ page report makes a good start. But IES, faced with limited time and resources to complete the many experiments being conducted within the Regional Education Lab system, put strict limits on the number of exploratory analyses researchers could conduct. We usually think of exploratory work as questions to follow up on puzzling or unanticipated results. However, in the case of the REL experiments, IES asked researchers to focus on a narrow set of “confirmatory” results and anything else was considered “exploratory,” even if the question was included in the original research design.

The strict IES criteria were based on the principle that when a researcher is using tests of statistical significance, the probability of erroneously concluding that there is an impact when there isn’t one increases with the frequency of the tests. In our evaluation of AMSTI, we limited ourselves to only four such “confirmatory” (i.e., not exploratory) tests of statistical significance. These were used to assess whether there was an effect on student outcomes for math problem-solving and for science, and the amount of time teachers spent on “active learning” practices in math and in science. (Technically, IES considered this two sets of two, since two were the primary student outcomes and two were the intermediate teacher outcomes.) The threshold for significance was made more stringent to keep the probability of falsely concluding that there was a difference for any of the outcomes at 5% (often expressed as p < .05).

While the logic for limiting the number of confirmatory outcomes is based on technical arguments about adjustments for multiple comparisons, the limit on the amount of exploratory work was based more on resource constraints. Researchers are notorious (and we don’t exempt ourselves) for finding more questions in any study than were originally asked. Curiosity-based exploration can indeed go on forever. In the case of our evaluation of AMSTI, however, there were a number of fundamental policy questions that were not answered either by the confirmatory or by the exploratory questions in our report. More research is needed.

Take the confirmatory finding that the program resulted in the equivalent of 28 days of additional math instruction (or technically an impact of 5% of a standard deviation). This is a testament to the hard work and ingenuity of the AMSTI team and the commitment of the school systems. From a state policy perspective, it gives a green light to continuing the initiative’s organic growth. But since all the schools in the experiment applied to join AMSTI, we don’t know what would happen if AMSTI were adopted as the state curriculum requiring schools with less interest to implement it. Our results do not generalize to that situation. Likewise, if another state with different levels of achievement or resources were to consider adopting it, we would say that our study gives good reason to try it but, to quote Lee Cronbach, a methodologist whose ideas increasingly resonate as we translate research into practice: “…positive results obtained with a new procedure for early education in one community warrant another community trying it. But instead of trusting that those results generalize, the next community needs its own local evaluation” (Cronbach, 1975, p. 125).

The explorations we conducted as part of the AMSTI evaluation did not take the usual form of deeper examinations of interesting or unexpected findings uncovered during the planned evaluation. All the reported explorations were questions posed in the original study plan. They were defined as exploratory either because they were considered of secondary interest, such as the outcome for reading, or because they were not a direct causal result of the randomization, such as the results for subgroups of students defined by different demographic categories. Nevertheless, exploration of such differences is important for understanding how and for whom AMSTI works. The overall effect, averaging across subgroups, may mask differences that are of critical importance for policy

Readers interested in the issue of subgroup differences can refer to Table 6.11. Once differences are found in groups defined in terms of individual student characteristics, our real exploration is just beginning. For example, can the difference be accounted for by other characteristics or combinations of characteristics? Is there something that differentiates the classes or schools that different students attend? Such questions begin to probe additional factors that can potentially be addressed in the program or its implementation. In any case, the report just released is not the “final report.” There is still a lot of work necessary to understand how any program of this sort can continue to be improved.

New RFP calls for Building Regional Research Capacity

The US Department of Education (ED) has just released the eagerly anticipated RFP for the next round of the Regional Education Laboratories (RELs). This RFP contains some very interesting departures from how the RELs have been working, which may be of interest especially to state and local educators.

For those unfamiliar with federal government organizations, the RELs are part of the National Center for Education Evaluation and Regional Assistance (abbreviated NCEE), which is within the Institute of Education Sciences (IES), part of ED. The country is divided up into ten regions, each one served by a REL—so the RFP announced today is really a call for proposals in ten different competitions. The RELs have been in existence for decades but their mission has evolved over time. For example, the previous RFP (about 6 years ago) put a strong emphasis on rigorous research, particularly randomized control trials (RCTs) leading the contractors in each of the 10 regions to greatly expand their capacity, in part by bringing in subcontractors with the requisite technical skills. (Empirical conducted or assisted with RCTs in four of the 10 regions.) The new RFP changes the focus in two essential ways.

First, one of the major tasks is building capacity for research among practitioners. Educators at the state and local levels told ED that they needed more capacity to make use of the longitudinal data systems that the ED has invested in through grants to the states. It is one thing to build the data systems. It is another thing to use the data to generate evidence that can inform decisions about policies and programs. Last month at the conference of the Society for Research on Educational Effectiveness, Rebecca Maynard, Commissioner of NCEE talked about building a “culture of experimentation” among practitioners and building their capacity for simpler experiments that don’t take so long and are not as expensive as those NCEE has typically contracted for. Her point was that the resulting evidence is more likely to be used if the practitioners are “up close and immediate.”

The second idea found in the RFP for the RELs is that each regional lab should work through “alliances” of state and local agencies. These alliances would cross state boundaries (at least within the region) and would provide an important part of the REL’s research agenda. The idea goes beyond having an advisory panel for the REL that requests answers to questions. The alliances are also expected to build their own capacity to answer these questions using rigorous research methods but applying them cost-effectively and opportunistically. The capacity of the alliances should outlive the support provided by the RELs. If your organization is part of an existing alliance and would like to get better at using and conducting research, there are teams being formed to go after the REL contracts that would be happy to hear from you. (If you’re not sure who to call, let us know and we’ll put you in touch with an appropriate team.)

Looking Back 35 Years to Learn about Local Experiments

With the growing interest among federal agencies in building local capacity for research, we took another look at an article by Lee Cronbach published in 1975. We found it has a lot to say about conducting local experiments and implications for generalizability. Cronbach worked for much of his career at Empirical’s neighbor, Stanford University, and his work has had a direct and indirect influence on our thinking. Some may interpret Cronbach’s work as stating that randomized trials of educational interventions have no value because of the complexity of interactions between subjects, contexts, and the experimental treatment. In any particular context, these interactions are infinitely complex, forming a “hall of mirrors” (as he famously put it, p. 119), making experimental results—which at most can address a small number of lower-order interactions—irrelevant. We don’t read it that way. Rather, we see powerful insights as well as cautions for conducting the kinds of field experiments that are beginning to show promise for providing educators with useful evidence.

We presented these ideas at the Society for Research in Educational Effectiveness conference in March, building the presentation around a set of memorable quotes from the 1975 article. Here we highlight some of the main ideas.

Quote #1: “When we give proper weight to local conditions, any generalization is a working hypothesis, not a conclusion…positive results obtained with a new procedure for early education in one community warrant another community trying it. But instead of trusting that those results generalize, the next community needs its own local evaluation” (p. 125).

Practitioners are making decisions for their local jurisdiction. An experiment conducted elsewhere (including over many locales, where the results are averaged) provides a useful starting point, but not “proof” that it will or will not work in the same way locally. Experiments give us a working hypothesis concerning an effect, but it has to be tested against local conditions at the appropriate scale of implementation. This brings to mind California’s experience with class size reduction following the famous experiment in Tennessee, and how the working hypothesis corroborated through the experiment did not transfer to a different context. We also see applicability of Cronbach’s ideas in the Investing in Innovation (i3) program, where initial evidence is being taken as a warrant to scale-up intervention, but where the grants included funding for research under new conditions where implementation may head in unanticipated directions, leading to new effects.

Quote #2: “Instead of making generalization the ruling consideration in our research, I suggest that we reverse our priorities. An observer collecting data in one particular situation…will give attention to whatever variables were controlled, but he will give equally careful attention to uncontrolled conditions…. As results accumulate, a person who seeks understanding will do his best to trace how the uncontrolled factors could have caused local departures from the modal effect. That is, generalization comes late, and the exception is taken as seriously as the rule” (pp. 124-125).

Finding or even seeking out conditions that lead to variation in the treatment effect facilitates external validity, as we build an account of the variation. This should not be seen as a threat to generalizability because an estimate of average impact is not robust across conditions. We should spend some time looking at the ways that the intervention interacts differently with local characteristics, in order to determine which factors account for heterogeneity in the impact and which ones do not. Though this activity is exploratory and not necessarily anticipated in the design, it provides the basis for understanding how the treatment plays out, and why its effect may not be constant across settings. Over time, generalizations can emerge, as we compile an account of the different ways in which the treatment is realized and the conditions that suppress or accentuate its effects.

Quote #3: “Generalizations decay” (p. 122).

In the social policy arena, and especially with the rapid development of technologies, we can’t expect interventions to stay constant. And we certainly can’t expect the contexts of implementation to be the same over many years. The call for quicker turn-around in our studies is therefore necessary, not just because decision-makers need to act, but because any finding may have a short shelf life.

Cronbach, L. J. (1975). Beyond the two disciplines of scientifi­c psychology. American Psychologist, 116-127.