A Constructive Look at Follow Through Results
Carl Bereiter, Ontario Institute for Studies in Education, and Midian Kurland, University of Illinois at Urbana-Champaign
Reprinted from Interchange, Vol. 12, Winter, 1981, with permission.
Follow Through is a large compensatory education program that operated in scores of communities across the United States throughout the seventies and that continues, on a reduced scale, today. During its most active phase, it was conducted as a massive experiment, involving planned variation of education approaches and collection of uniform data at each site. The main evaluation of outcomes was carried out by Abt Associates, Inc. (a private consulting firm, based in Cambridge, Massachusetts) on the second and third cohorts of children who reached third grade in the program, having entered in kindergarten or first grade. In a series of voluminous reports, Abt Associates presented analyses indicating that among the various education approaches tried, only those emphasizing “basic skills” showed positive effects when compared to Non-Follow Through treatments. House, Glass, McLean, and Walker (1978a) published a critique of the Abt Associates evaluation, along with a small reanalysis that found essentially no significant differences in effectiveness among the planned variations in educational approaches. Because of the great social importance attached to educational programs for disadvantaged groups and because no other large-scale research on the topic is likely to materialize in the near future, the Follow Through experiment deserves continuing study. The study reported here is an attempt, through more sharply focused data analysis, to obtain a more definitive answer to the question of whether different educational approaches led to different achievement outcomes.
Is it possible that the Follow Through planned variation experiment has yielded no findings of value? Is it possible, after years of effort and millions of dollars spent on testing different approaches, that we know nothing more than we did before about ways to educate disadvantaged children? This is the implicit conclusion of the widely publicized critique by House, Glass, McLean, and Walker (1978a, 1978b). House et al found no evidence that the various Follow Through models differed in effectiveness from one another or from Non-Follow Through programs. The only empirical finding House et al were willing to credit was that there was great variation in results from one Follow Through site to another. This conclusion, as we shall show, is no more supportable than the conclusions House et al rejected. Accordingly, if we were to follow House, Glass, McLean, and Walker’s lead, we should have to conclude that there are no substantive findings to be gleaned from the largest educational experiment ever conducted.
It would be a serious mistake, however, to take the critique by House et al as any kind of authoritative statement about what is to be learned from Follow Through. The committee assembled by House was charged with reviewing the Abt Associates evaluation of Follow Through (Stebbins et al, 1977), not with carrying out an inquiry of their own. More or less, the committee stayed within the limits of this charge, criticizing a variety of aspects of the design, execution, and data analysis of the experiment. Nowhere in their report do the committee take up the constructive problem that Abt Associates had to face or that any serious inquiries will have to face. Given the weaknesses of the Follow Through experiment, how can one go about trying to extract worthwhile findings from it?
In this paper we try to deal constructively with one aspect of the Follow Through experiment: the comparison of achievement test results among the various sponsored approaches. We try to show that if this comparison is undertaken with due cognizance of the limitations of the Follow Through experiment, it is possible to derive some strong, warranted, and informative conclusions. We do not present our research as a definitive, and certainly not as a complete, inquiry into Follow Through results. We do hope to show, however, that the conclusion implied by the House committee-that the Follow Through experiment is too flawed to yield any positive findings-is gravely mistaken.
Delimiting the Problem
Although Project Follow Through has numerous shortcomings as an experiment, the seriousness of these shortcomings varies greatly depending on what questions are asked of the data. One shortcoming was in the outcome measures used, particularly in their limited range compared to the range of objectives pursued by Follow Through sponsors. The House committee devotes the largest part of its critique to this shortcoming, although it is a shortcoming that limits only the range of conclusions that may be drawn. House et al allow, for instance, that the Metropolitan Achievement Test was “certainly a reasonable choice for the material it covers” (1978a, p. 138). Accordingly, Follow Through’s shortcomings as to outcome measures ought not to stand in the way of answering questions that are put in terms appropriate to the measures that were used.
Another shortcoming, recognized by all commentators on Follow Through, is the lack of strictly comparable control groups. Follow Through and Non-Follow Through groups at the same site differed from one another in uncontrolled and only partly measurable ways, and the differences themselves varied from site to site. This circumstance makes it difficult to handle questions having to do with whether children benefited from being in Follow Through, because such questions require using Non-Follow Through data as a basis for inferring how Follow Through children would have turned out had they not been in Follow Through.
Much of the bewildering complexity of the Abt Associates’ analyses results from attempts to make up statistically for the lack of experimental comparability. We do not intend to examine those attempts except to note one curiosity. The difficulty of evaluating “benefits” holds whether one is asking about the effects of Follow Through as a whole, the effects of a particular model, or the effect of a Follow Through program at a single site. The smaller the unit, however, the more vulnerable the results are likely to be to a mismatch between Follow Through and Non-Follow Through groups. On the one hand, to the extent that mismatches are random, they should tend to average out in larger aggregates. On the other hand, at a particular site, the apparent success or failure of a Follow Through program could depend entirely on a fortuitously favorable or unfavorable match with a Non-Follow Through group.
For unknown reasons, both the Abt Associates and the House committee analysts have assumed the contrary of the point just made. While acknowledging, for instance, that the prevalence of achievement test differences in favor of Non-Follow Through groups could reflect mismatch, they are able to make with confidence statements like “Seven of the ten Direct Instruction sites did better than the comparison classes but three of the Direct Instruction sites did worse” (House et al, 1978a, p. 154). Such a statement is nonsense unless one believes that at each of the ten sites a valid comparison between Follow Through and Non-Follow Through groups could be made. But if House et al believe that, how could they then believe that the average of those ten comparisons is invalid? This is like arguing that IQ tests give an invalid estimate of the mean intelligence level of disadvantaged children and then turning around and using those very tests to classify individual disadvantaged children as retarded.
There is an important class of questions that may be investigated, however, without having to confront the problem of comparability between Follow Through and Non-Follow Through groups. These are questions involving the comparison of Follow Through models with one another. A representative question of this kind would be-how did the Follow Through models compare with one another in reading achievement test scores at the end of third grade? There are problems in answering such a question, but the lack of appropriate control groups is not one of them. We can, if we choose, simply ignore the Non-Follow Through groups in dealing with questions of this sort.
Questions about the relative performance of different Follow Through models are far from trivial. The only positive conclusions drawn by Abt Associates relate to questions of this kind, and the House committee’s report is largely devoted to disputing those conclusions -that is, disputing Abt’s conclusions that Follow Through models emphasizing basic skills achieved better results than others in basic skills and in self-concept. The models represented in Follow Through cover a wide range of educational philosophies and approaches to education. Choose any dimension along which educational theories differ and one is likely to find Follow Through models in the neighborhood of each extreme. This is not to say that the Follow Through models are so well distinguished that they provide clean tests of theoretical issues in education. But the differences that are there-like, for instance, the difference between an approach based on behavior modification principles and an approach modeled on the English infant school-offer at least the possibility of finding evidence relevant to major ideological disputes within education.
Unscrambling the Methodology
The Abt Associates analysts were under obligation to try to answer the whole range of questions that could be asked about Follow Through effects. In order to do this in a coherent way, they used one kind of statistic that could be put to a variety of uses. This is the measure they called “effect size,” an adjusted mean difference between the Follow Through and Non-Follow Through subjects at a site. Without getting into the details of how effect size was computed, we may observe that this measure is more suitable for some purposes than for others. For answering question about benefits attributable to Follow Through, some such measure as effect size is necessary. For comparing one Follow Through model with another, however, the effect size statistic has the significant disadvantage that unremoved error due to mismatch between a Follow Through and Non-Follow Through group is welded into the measure itself. As we noted in the preceding section, comparisons of the effectiveness of Follow Through models with one another do not need to involve Non-Follow Through data. Because effect size measures will necessarily include some error due to mismatch (assuming that covariance adjustments cannot possibly remove all such error), these measures will contain “noise” that can be avoided when making comparisons among Follow Through models.
The Abt Associates analysts used several different ways of computing effect size, the simplest of which is called the “local” analysis. This method amounts to using the results for each cohort of subjects at each site as a separate experiment, carrying out a covariance analysis of Follow Through and Non-Follow Through differences as if no other sites or cohorts existed. Although this analysis has a certain elegance, it clearly does not take full advantage of the information available; the “pooled” analysis used by Abt, which uses data on whole cohorts to calculate regression coefficients and at the same time includes dummy variables to take care of site-specific effects, is much superior in this respect. The House committee, however, chose to use effect size measures based on the “local” analysis in their own comparison of models. In doing so, they used the least powerful of the Abt effect size measures, all of which are weakened (to unknown degrees) by error due to mismatch.
In their comparisons of Follow Through models, Abt Associates analysts calculated the significance of effects at different sites, using individual subjects at the sites as the units of analysis, and then used the distribution of significant positive and negative effects as an indicator of the effectiveness of the models. The House committee argued, on good grounds we believe, that the appropriate unit of analysis should have been sites rather than individual children. To take only the most obvious argument on this issue, the manner of implementing a Follow Through model is a variable of great presumptive significance, and it is most reasonably viewed as varying from site to site rather than from child to child. Having made this wise decision, however, the House committee embarked on what must be judged either an ill-considered or an excessively casual reanalysis of Follow Through data. Although the reanalysis of data by the House committee occupies only a small part of their report and is presented by them with some modesty, we believe their reanalysis warrants severe critical scrutiny. Without that reanalysis, the House committee’s report would have amounted to nothing more than a call for caution in interpreting the findings of the Abt Associates analysts. With the reanalysis, the House committee seems to be declaring that there are no acceptable findings to be interpreted. Thus a great deal hinges on the credibility of their reanalysis.
Let us therefore consider carefully what the House committee did in their reanalysis. First, they used site means rather than individual scores as the unit of analysis. This decision automatically reduced the Follow Through planned variation experiment from a very large one, with an N of thousands, to a rather small one, with an N in the neighborhood of one hundred. As previously indicated, we endorse this decision. However, it seems to us that when one has opted to convert a large experiment into a small one, it is important to make certain adjustments in strategy. This the House committee failed to do. If an experiment is very large, one can afford to be cavalier about problems of power, since the large N will presumably make it possible to detect true effects against considerable background noise. In a small experiment, one must be watchful and try to control as much random error as possible in order to avoid masking a true effect.
However, instead of trying to perform the most powerful analysis possible in the circumstances, the House committee weakened their analysis in a number of ways that seem to have no warrant. First, they chose to compare Follow Through models on the basis of Follow Through/Non-Follow Through differences, thus unnecessarily adding error variance associated with the Non-Follow Through groups. Next, they chose to use adjusted differences based on the “local” analysis, thus maximizing error due to mismatch. Next, they based their analysis on only a part of the available data. They excluded data from the second kindergarten-entering cohort, one of the largest cohorts, even though these data formed part of the basis for the conclusions they were criticizing. This puzzling exclusion reduced the number of sites considered, thus reducing the likelihood of finding significant differences. Finally, they divided each effect-size score by the standard deviation of test scores in the particular cohort in which the effect was observed. This manipulation served no apparent purpose. And minor though its effects may be, such as they are would be in the direction of adding further error variance to the analysis.
The upshot of all these methodological choices was that, while the House group’s reanalysis largely confirmed the ranking of models arrived at by Abt Associates, it showed the differences to be small and insignificant. Given the House committee’s methodology, this result is not surprising. The procedures they adopted were not biased in the sense of favoring one Follow Through model over another; hence it was to be expected that their analysis, using the same effect measures as Abt, would replicate the rankings obtained by Abt. (The rank differences shown in Table 7 of the House report are probably mostly the result of the House committee’s exclusion of data from one of the cohorts on which the Abt rankings were based.) On the other hand, the procedures adopted by the House committee all tended in the direction of maximizing random error, thus tending to make differences appear small and insignificant.
The analysis to be reported here is of the same general type as that carried out by the House committee. Like the House committee, we use site means rather than scores for individuals as the unit of analysis. The differences in procedure all arise from our effort to minimize random error and thus achieve the most powerful analysis possible. The following are the main differences between our analysis and the House et al analysis:
1. We used site means for Follow Through groups as the dependent variable, using other site-level scores as covariates. The House committee used locally adjusted site-level differences between Follow Through and Non-Follow Through groups as the dependent variable, with covariance adjustments having been made on an individual basis. Our procedure appears to have been endorsed in advance by the House committee. They state: “For the sake of both inferential validity and proper covariance adjustment, the classroom is the appropriate unit of analysis” (House et al, 1978a, p. 153). While the House committee followed their own prescription in using site-level scores as dependent variables, they failed to follow it when it came to covariance adjustments.
2. When we used Non-Follow Through scores, we entered them as covariates along with other covariates. The procedure adopted by the House committee amounted, in effect, to arbitrarily assigning Non-Follow Through mean scores a regression weight of 1 while giving all other variables empirically determined regression weights. We could not see any rational basis for such a deviation from ordinary procedures for statistical adjustment.
3. We combined all data from one site as a single observation, regardless of cohort. The House committee appear to have treated different cohorts from the same site as if they were different sites. This seemed to us to violate the rationale for analyzing data at the site level in the first place.
4. We restricted the analysis to models having data on 6 or more sites. To include in the analysis models having as few as 2 sites, as the House committee did, would, it seemed to us, reduce the power of the statistical tests to an absurd level.
The data analysis that followed from the above-mentioned decisions was quite straightforward and conventional. The dependent variable was always the mean score for a site on one or more Metropolitan Achievement Test subtests, averaged over all subjects in cohorts II and III for whom data were reported in the Abt Associates reports. Models, which ranged from 12 to 6 in number of sites, were compared by analysis of covariance, using some or all of the following covariates:
SES-An index of socio-economic status calculated by Abt for each cohort at each site. When more than one cohort represented a site, an n-weighted mean was computed.
EL-An index of ethnic and linguistic difference from the mainstream-treated in a manner similar to SES.
WRAT-Wide-range Achievement Test, administered near time of entry to Follow Through students. Taken as a general measure of academic readiness.
NFT-Mean score of local Non-Follow Through students on the dependent variable under analysis. As a covariate, NFT scores may be expected to control for unmeasured local or regional characteristics affecting scholastic achievement.
Two other covariates were tried to a limited extent: Raven Progressive Matrices scores (which, though obtained after rather than before treatment, might be regarded as primarily reflecting individual differences variance not affected by treatment) and a score indicating the number of years of Follow Through treatment experienced by subjects at a site (most Follow Through groups entered in kindergarten, thus receiving four years of Follow Through treatment; but some entered in first grade and received only three years). Our overall strategy for use of analysis of covariance was as follows: recognizing that reasonable cases could be made for and against the use of this covariate or that, we would try various combinations and, in the end, would take seriously only those results that held up over a variety of reasonable covariate sets.
Differences in achievement test performance-Two analyses of covariance will be reported here, with others briefly summarized. Figure 1 displays adjusted and standardized means from what we call the “full” analysis of covariance-that is, an analysis using the four main covariates (SES, EL, WRAT, and NFT) described in the preceding section. The virtue of this analysis is that it controls for all the main variables that previous investigators have tried, in one way or other, to control for in comparing Follow Through models.
Table 1* notes pair-wise differences which are significant at the .05 level by Newman-Keuls tests.
Figure 2* and Table 2* show comparable data for what we call the “conservative” analysis.
This analysis is conservative in the sense that it eliminates covariates for which there are substantial empirical and/or rational grounds for objection. Grounds for objecting to the NFT variable as a covariate have been amply documented in Abt reports and echoed in the report of the House committee (House et al, 1978a); they will not be repeated here. Use of WRAT as a covariate has been objected to on grounds that it is not, as logically required, antecedent to treatment (Becker & Carnine, Ref. Note 1)-that is, the WRAT, though nominally a pretest, was in fact administered at a time when at least one of the models had already purportedly taught a significant amount of the content touched on by the WRAT. While we would not suppose the SES and EL variables to be above reproach, we have not encountered criticisms suggesting their use would seriously bias results-whereas not to control for these variables would unquestionably leave the results biased in favor of models serving less disadvantaged populations. Accordingly, we have chosen them as the conservative set of covariates.
Other analyses, not reported, used different combinations of covariates from among those mentioned in the preceding section. In every case, these analyses yielded adjusted scores intermediate between those obtained from the “full” and the “conservative” analyses. Consequently, the results shown in Figures 1 and 2 may be taken to cover the full range of those observed.
In every analysis, differences between models were significant at or beyond the .05 level on every achievement variable-almost all beyond the .01 level. As Figures 1 and 2 show, models tended to perform about the same on every achievement variable. Thus there is little basis for suggesting that one model is better at one thing, another at another.
The relative standing of certain models, particularly the Tucson Early Education Model, fluctuated considerably depending on the choice of covariates.1 Two models, however, were at or near the top on every achievement variable, regardless of the covariates used; these were Direct Instruction and Behavior Analysis. Two models were at or near the bottom on every achievement variable, regardless of the covariates used; these were the EDC Open Education Model and Responsive Education. Differences between the two top models and the two bottom models were in most cases statistically significant by Newman-Keuls tests.
Variability between sites-The only empirical finding that the House committee was willing to credit was that there was enormous variability of effects from site to site within Follow Through models. In their words: “Particular models that worked well in one town worked poorly in another. Unique features of the local settings had more effect on achievement than did the models” (House et al, 197&, p. 156). This conclusion has recently been reiterated by the authors of the Abt evaluation report (St. Pierre, Anderson, Proper, & Stebbins, 1978) in almost the same words.
The ready acceptance of this conclusion strikes us as most puzzling. It is conceivable that all of the variability between sites within models is due to mismatch between Follow Through and Non-Follow Through groups. This is unlikely, of course, but some of the variability between sites must be due to this factor, and unless we know how much, it is risky to make statements about the real variability of effects. Furthermore there is, as far as we are aware, no evidence whatever linking achievement to “unique features of the local setting.” This seems to be pure conjecture-a plausible conjecture, no doubt, but not something that should be paraded as an empirical finding.
Our analyses provide some basis for looking at the between-site variability question empirically. Follow Through sites varied considerably in factors known to be related to achievement-socioeconomic status, ethnic composition, WRAT pretest scores, etc. To say that the variance in achievement due to these factors was greater than the variance due to model differences may be true but not very informative. It amounts to nothing more than the rediscovery of individual differences and is irrelevant to the question of how much importance should be attached to variation among Follow Through models. To say that differences in educational method are trivial because their effects are small in comparison to the effect of demographic characteristics is as absurd as saying that diet is irrelevant to children’s weight because among children weight variations due to diet are small in comparison to weight variations due to age.
Standardized adjusted mean Metropolitan Achievement Test scores obtained from “full” covariance analysis (rounded to the nearest even tenth).
The variability issue may be more cogently formulated as follows: considering only the variance in achievement that cannot be accounted for by demographic and other entering characteristics of students, what part of that variance can be explained by differences in Follow Through models and what part remains unexplained? Our analyses provide an approximate answer to this question, since covariance adjustments act to remove variance among sites due to entering characteristics. Depending on the achievement test variable considered and on the covariates used, we found model differences to account for roughly between 17 and 55 per cent of the variance not attributable to covariates (as indexed by w2).
Standardized adjusted mean Metropolitan Achievement Test scores obtained from “conservative” covariance analysis (rounded to the nearest even tenth).
These results are shown graphically in Figures 1 and 2. Adjusted mean scores are displayed there in units of the standard deviation of residual site means. Thus, to take the most extreme case, in Figure 2 the adjusted mean score of Direct Instruction sites on Language Part B is 3.6 standard deviations above the adjusted mean score of EDC Open Education sites-that is, 3.6 standard deviations of between-site residual variability; in other words, an enormous difference compared to differences between sites within models. That is the most extreme difference, but in no case is the adjusted difference between highest and lowest model less than 1.4 standard deviations. Although what constitutes a “large” effect must remain a matter of judgment, we know of no precedent according to which treatment effects of this size could be considered small in relation to the unexplained variance.
Treatment effects on other variables-Although the principal concern of this study was with achievement test differences, the method of analysis is adaptable to studying differences in other outcomes as well. Accordingly we ran several briefer analyses, looking at what Abt Associates call “cognitive / conceptual” and “affective” outcomes.
Two kinds of measures used in the Follow Through evaluation were regarded by Abt Associates as reflecting “cognitive / conceptual” outcomes- Raven’s Progressive Matrices (a nonverbal intelligence test) and several Metropolitan subtests judged to measure indirect cognitive consequences of learning. The House committee objected to Progressive Matrices on grounds that is insensitive to school instruction. This rather begs the question of effects of cognitively-oriented teaching, however. True, Progressive Matrices performance may be insensitive to ordinary kinds of school instruction, but does that mean it will be insensitive to novel instructional approaches claiming to be based on cognitive theories and declaring such objectives as “the ability to reason” and “logical thinking skills in four major cognitive areas (classification, seriation, spatial relations and temporal relations)”? It seems that this should be an empirical question.
If it is an empirical question, the answer is negative. Using the same kinds of covariance analyses as were used on the achievement test variables, we found no statistically significant differences between Follow Through models in Progressive Matrices performance. This finding is consistent with the Abt Associates’ analyses, which show few material effects on this test, and more negative than positive ones.
Among Metropolitan subtests the most obviously “cognitive” are Reading (which is, in effect, paragraph comprehension) and Mathematics Problem-Solving. As indicated in Figures 1 and 2, our analyses show differences among models on these subtests that are similar in trend to those found on the other subtests. They tend, however, to be of lesser magnitude. The most obvious explanation for the lesser magnitude of difference on these subtests is the same as that offered by House et al for the absence of differences on Progressive Matrices-that these subtests, reflecting more general differences in intellectual ability, are less sensitive to instruction. There is, however, a further hypothesis that should be tested. Conceivably, certain models-let us say those that avowedly emphasize “cognitive” objectives-are doing a superior job of teaching the more cognitive aspects of reading and mathematics, but the effects are being obscured by the fact that performance on the appropriate subtests depends on mechanical proficiency as well as on higher-level cognitive capabilities. If so, these hidden effects might be revealed by using performance on the more “mechanical” subtests as covariates.
This we did. Model differences in Reading (comprehension) performance were examined, including Word Knowledge as a covariate. Differences in Mathematics Problem Solving were examined, including Mathematics Computation among the covariates. In both cases the analyses of covariance revealed no significant differences among models. This is not a surprising result, given the high correlation among Metropolitan subtests. Taking out the variance due to one subtest leaves little variance in another. Yet it was not a forgone conclusion that the results would be negative. If the models that proclaimed cognitive objectives actually achieved those objectives, it would be reasonable to expect those achievements to show up in our analyses.
The same holds true for performance on the affective measures included in the Follow Through evaluation. The Abt Associates’ analyses show that the ranking of models on affective measures corresponds closely to their ranking on achievement measures. House et al point out, however, that the instruments used place heavy demands on verbal skills. Conceivably, therefore, if reading ability were controlled statistically, the results might tell a different story. We analyzed scores on the Coopersmith Self-Concept Inventory, including reading subtest scores along with the other covariates. The result showed no significant difference among models on the Coopersmith. This finding could mean either that there are no differences between models in effects on self-concept or that self-concept among disadvantaged third-graders is sufficiently dependent on reading ability that, when one statistically removes reading ability differences, one at the same time removes genuine self-concept differences. We know of no way to resolve this ambiguity with the available data. One thing is clear, however: removing effects due to reading achievement does not in any way yield results either favoring models that emphasize self-concept or disfavoring models that emphasize academic objectives.
Before attempting to give any interpretation of Follow Through results, we must emphasize the main finding of our study-that there were results. Follow Through models were found to differ significantly on every subtest of the Metropolitan Achievement Test.
Let us briefly compare our findings with those of Abt Associates and the House committee.
1. We disagree with both Abt and House et al in that we do not find variability among sites to be so great that it overshadows variability among models. It appears that a large part of the variability observed by Abt and House et al was due to demographic factors and experimental error. Once this variability is brought under control, it becomes evident that differences between models are quite large in relation to the unexplained variability within models.
2. Our findings on the ranking of Follow Through models on achievement variables are roughly in accord with those of the House Committee, but we differ from the House committee in finding significant differences among models on all achievement variables whereas they found almost none. The similarities are no doubt due to the fact that the two analyses used the same basic units-site-level means. The difference in significance of outcomes is apparently due to the variety of ways (previously discussed) in which our analysis was more powerful than theirs.
3. The Abt Associates’ results indicate that among major Follow Through models, there is only one “winner” in the sense of having a preponderance of positive effects-namely, Direct Instruction. All other models showed predominately null or negative effects. Our results are not exactly comparable in that we compared Follow Through models only with one another and not with Non-Follow Through groups; consequently we cannot speak of “positive” or “negative” effects. However, our results show two models to be above average on all achievement subtests and two models to be below average on all subtests. Thus our results may be said to indicate two “winners”-Direct Instruction and Behavior Analysis- and two “losers”-EDC Open Education and Responsive Education.
We put the words “winners” and “losers” in quotation marks because, of course, Follow Through was not a contest with the object of attaining the highest possible achievement test scores. It simply happens that the outcomes on which Follow Through models are found to differ are achievement test scores. That other criteria might have shown different winners and losers (a point heavily emphasized by the House committee) must remain a conjecture for which all the available evidence is negative. What we have are achievement test differences, and we must now turn to the question of what those differences might mean.
It lies outside the scope of this paper to discuss the importance of scholastic achievement itself. The more immediate issue is whether the observed differences in achievement test scores reflect actual differences in mastery of reading, mathematics, spelling, and language.
One obvious limitation that must be put on the results is that the Metropolitan Achievement Test, like all other standardized achievement batteries, covers less than the full range of achievement objectives. As House et al point out, the test does not cover “even such straightforward skills as the ability to read aloud, to write a story, or to translate an ordinary problem into numbers” (1978b, p. 473). This much is certainly true, but House et al then go on to say, “it would be reckless to suppose that the results of the testing indicate the attainment of these broader goals” (p. 473). “Reckless” is far too strong a word here.2 From all we know about the intercorrelation of scholastic skills, one could be fairly confident in assuming that children who perform above average on the MAT would also perform above average on tests of the other skills mentioned. A glance again at Figures 1 and 2 tells us that achievements in a variety of areas tend to go together. Given the homogeneous drift of scores downward from left to right in those figures, it is hard to imagine another set of achievement measures in mathematical and language skills that would show a trend in the opposite direction. Such a trend cannot be declared impossible, of course, but if House et al expect us to take such a possibility seriously, then they ought to provide some evidence to make it plausible.
A more serious kind of charge is that the MAT is biased in favor of certain kinds of programs. If true, this could mean that the observed test score differences between models reflect test bias and not true differences on the achievement variables that the test is supposed to measure. We must be very careful, however, in using the term bias. One sometimes hears in discussions of Follow Through statements that the MAT is biased in favor of models that teach the sort of content measured by the MAT. This is a dangerous slip in usage of the word bias and must be avoided. It makes no sense whatever to call it bias when an achievement test awards higher scores to students who have studied the domain covered by the test than to students who have not. It would be a very strange achievement test if it did not.
It is meaningful, however, to say that an achievement test is biased in its sampling of a domain of content, but even here one must be careful not to abuse the term. The Mathematics Concept subtest of the MAT, for instance, is a hodge-podge of knowledge items drawn from “old math,” “new math,” and who knows what. For any given instructional program, it will likely be found that the test calls for knowledge of material not covered by that program-but that doesn’t mean the test is biased against the program. The test obviously represents a compromise that cannot be fully satisfactory to any program. The only ground for a charge of bias would be that the compromise was not even-handed. Investigating such a charge would require a thorough comparison of content coverage in the test and content coverage in the various Follow Through programs. It does no good to show that for a particular program there are discrepancies between content covered and content tested. The same might be equally true of every program.
As far as the Follow Through evaluation goes, the only MAT subtest to which a charge of content bias might apply (we have no evidence that it does) is Mathematics Concepts. The other subtests all deal with basic skills in language and mathematics. Different programs might teach different methods of reading or doing arithmetic, and they might give different amounts of emphasis to these skills, but the skills tested on the MAT are all ones that are appropriate to test regardless of the curriculum. Even if a particular Follow Through model did not teach arithmetic computation at all, it would still be relevant in an assessment of that program to test students’ computational abilities; other people care about computation, even if the Follow Through sponsor does not. The reason why Mathematics Concepts may be an exception is that, while everyone may care about mathematical concepts, different people care about different ones, and so a numerical score on a hodge-podge of concepts may not be informative.
While such skill tests as those making up the bulk of the MAT are relatively immune to charges of content bias, they can be biased in other ways. They may, perhaps, be biased in the level of cognitive functioning that they tap within a skill area. The House committee implies such a bias when they say, “the selection of measures favors models that emphasize rote learning of the mechanics of reading, writing, and arithmetic” (House et al, 1978a, p. 14S). This is a serious charge and, if true, would go some way toward discrediting the findings.
But House et al offer no support for this charge, and on analysis it seems unlikely that they could. Their statement rests on three assumptions for which we know of no support: (1) That “the mechanics of reading, writing, and arithmetic” can be successfully taught by rote; (2) that there were Follow Through models that emphasized rote learning (the model descriptions provided by Abt give no suggestion that this is true)3 and (3) that the MAT measures skills in such a way that the measurement favors children who have learned those skills by rote rather than through a meaningful process. We must conclude, in fact, that since the House committee could not have been so naive as to hold all three of these assumptions, they must have introduced the word “rote” for rhetorical effect only. Take the word out and their statement reduces to an unimpressive complaint about the limited coverage of educational objectives in the Follow Through evaluation.
A final way in which skill tests might be biased is in the form of the test problems. Arithmetic computation problems, for instance, might be presented in notation that was commonly employed in some programs and not in others; or reading test items might use formats similar to those used in the instructional materials of one program and not another. Closely related to this is the issue of “teaching for the test”-when this implies shaping the program to fit incidental features of a test such as item formats. We may as well throw in here the issue of test-wiseness itself as a program outcome-that is, the teaching of behaviors which, whether intended to do so or not, help children perform well on tests-since it bears on the overall problem of ways in which a program might achieve superior test scores without any accompanying superiority in actual learning of content. In short, children in some programs might simply get better at taking tests.
If one looks at the Direct Instruction and Behavior Analysis models, with their emphasis on detailed objectives and close monitoring of student progress, and compares them to EDC Open Education, with its disavowal of performance objectives and repudiation of standardized testing, it is tempting to conclude in the absence of any evidence that the former models must surely have turned out children better prepared to look good on tests, regardless of the children’s true states of competence. Without wishing to prejudge the issue, we must emphasize that it is an empirical question to what extent children schooled in the various Follow Through models were favored or disfavored with respect to the process of testing itself.
In general, children involved in the Follow Through evaluation were subjected to more standardized testing than is normal. Since studies of test-wiseness indicate rapidly diminishing returns from increasing amounts of familiarization with testing (Cronbach, 1960), there is presumptive evidence against claims that differential amounts of test-taking among models could be significant in accounting for test-score differences. It should be possible to investigate this matter with Follow Through data, though not from the published data. Children in the final Follow Through evaluation had been subjected to from two to five rounds of standardized testing. Accordingly it should be possible to evaluate the effect of frequency of previous testing on third-grade test scores.
There are, however, numerous ways in which Follow Through experience could affect children’s behavior during testing. The amount of experience that children in any program had with actual test-taking is probably trivial in comparison to the amount of experience some children got in doing workbook pages and similar sorts of paper-and-pencil activities. And the nature of these activities might have varied from ones calling for constructed responses, quite unlike those on a multiple-choice test, to ones that amounted virtually to a daily round of multiple-choice test-taking. Programs vary not only in the amount of evaluation to which children are subjected but also in the manner of evaluationp;be it covert, which might have little effect on the children, or face-to-face and oral, or carried out through group testing. Finally, given that testing conditions in the Follow Through evaluation were not ideal, it is probably relevant how well children in the various programs learned to cheat effectivelyp;that is, to copy from the right neighbor.
Some or most of these variables could be extracted from available information, and it would be then possible to carry out analyses showing the extent to which they account for test scores and for the score differences between models. Only through such a multivariate empirical investigation could we hope to judge how seriously to take suggestions that the score differences among models were artifactual. Until that time, insinuations about “teaching for the test” must be regarded as mere prejudice.
What Do The Results Mean?
What we have tried to establish so far is that there are significant achievement test differences between Follow Through models and that, so far as we can tell at present, these test score differences reflect actual differences in school learning. Beyond this point, conclusions are highly conjectural. Although our main purpose in this paper has been simply to clarify the empirical results of the Follow Through experiment, we shall venture some interpretive comments, if for no other purpose than to forestall possible misinterpretations.
The two high-scoring models according to our analysis are Direct Instruction and Behavior Analysis; the two low-scoring are EDC Open Education and Responsive Education. If there is some clear meaning to the Follow Through results, it ought to emerge from a comparison of these two pairs of models. On the one hand, distinctive characteristics of the first pair are easy to name: sponsors of both the Direct Instruction and Behavior Analysis models call their approaches “behavioral” and “structured” and both give a high priority to the three R’s. EDC and Responsive Education, on the other hand, are avowedly “child-centered.” Although most other Follow Through models could also claim to be child-centered, these two are perhaps the most militantly so and most opposed to what Direct Instruction and Behavior Analysis stand for.
Thus we have, if we wish it, a battle of the philosophies, with the child-centered philosophy coming out the loser on measured achievement, as it has in a number of other experiments (Bennett, 1976; Stallings, 1975; Bell and Switzer, 1973; Bell, Zipousky & Switzer, 1976). This is interesting if one is keen on ideology, but it is not very instructive if one is interested in improving as educational program. Philosophies don’t teach kids. Events teach kids, and it would be instructive to know what kinds of events make the difference in scholastic achievement that we have observed.
The teaching behavior studies of Brophy & Good (1974), Rosenshine (1976), and Stallings & Kaskowitz (1974) are helpful on this point. Generally they contrast direct with informal teaching styles, a contrast appropriate to the two kinds of models we are comparing. Consistently it is the more direct methods, involving clear specifications of objectives, clear explanations, clear corrections of wrong responses, and a great deal of “time on task,” that are associated with superior achievement test performance. The effects tend to be strongest with disadvantaged children.
These findings from teacher observation studies are sufficiently strong and consistent that we may reasonable ask what if anything Follow Through results add to them. They add one very important element, the element of experimental change. The teacher observation studies are correlational. They show that teachers who do x get better achievement results than those who do y. The implication is that if the latter teachers switched from doing y to doing x, they would get better results, too; but correlational studies can’t demonstrate that. Perhaps teachers whose natural inclination is to do y will get worse results if they try to do x. Or maybe teachers who do y can’t or worse won’t do x. Or maybe x and y don’t even matter; they only serve as markers for unobserved factors that really make the difference.
The Follow Through experiment serves, albeit imperfectly, to resolve these uncertainties. Substantial resources were lavished on seeing to it that teachers didn’t just happen to use direct or informal methods according to their inclinations by rather that they used them according to the intent of the model sponsors. The experimental control was imperfect because communities could choose what Follow Through model to adopt, and in some cases, we understand, teachers could volunteer to participate. Nevertheless, it seems safe to assume that there was some sponsor effect on teacher behavior in all instances, so that some teachers who would naturally do x were induced to do y and vise-versa. Thus, with tentativeness, we can infer from Follow Through results that getting teachers of disadvantaged children to use more direct instructional methods as opposed to more informal ones will lead to superior achievement in commonly tested basic skills.
Before concluding, however, that what accounts for the superior achievement test scores of Direct Instruction and Behavior Analysis sites is their use of direct teaching methods, we should consider a more profound way in which these two models are distinguished from the others. These models are distinctive not only at the level of immediately observable teacher behavior but also at a higher level which may be called the systemic. One may observe a lesson in which the teacher manifests all the usual signs of direct teaching- lively manner, clear focus on instructional objectives, frequent eliciting of response from students, etc. One may return weeks later to find the same teacher with the same class manifesting the same direct teaching behavior-and still teaching the same lesson! The fault here is at the systemic level: the teacher is carrying out sorts of activities that should result in learning but is failing to organize and regulate them in such a way as to converge on the intended objectives.
More effective teachers-and this includes the great majority- function according to a convergent system. Consider a bumbling Mr. Chips introducing his pupils to multiplication by a two-digit multiplier. He demonstrates the procedure at the chalkboard and then discovers that most of the students cannot follow the procedure because they have forgotten or never learned their multiplication facts. So he backs up and reviews these facts, then demonstrates the algorithm again and assigns some practice problems. Performance is miserable, so he teaches the lesson again. By this time some children get it, and they teach others. With a bit of help, most of the class catches on. Mr. Chips then gives special tutoring, perhaps with use of supplementary concrete materials, to the handful of students who haven’t yet got it. Finally everyone has learned the multiplication algorithm except for the slowest pupils in the class-who, as a matter of fact, haven’t yet learned to add either.
Although none of the procedures used by Mr. Chips are very efficient, he applies them in a convergent way so that eventually almost all the children reach the instructional objective. Some of his procedures may not have a convergent effect at all. For instance, he may assign practice worksheets to pupils who haven’t yet grasped the algorithm, and the result is that they merely practice their mistakes (a divergent activity). But the overall effect is convergent. Given more efficient activities, convergence on the instructional goal might be more rapid and it might include the pupils who fail at the hands of Mr. Chips. But the difference in effectiveness, averaged over all pupils, would probably not be great. This convergent property of teaching no doubt contributes, as Stephens (1967) has suggested, to the scarcity of significant differences between teaching methods. Unless severely constrained, most teachers will see to it that, one way or another, their students reach certain goals by the end of the term.
We suggest that teaching performance of the kind just described be taken as baseline and that innovative educational practices, such as those promoted by the Follow Through sponsors, be judged in relation to that baseline. What would happen to the teaching of our Mr. Chips if he came under the supervision of a Follow Through sponsor? It seems fairly clear that his system for getting students to reach certain goals by the end of the term would be enhanced if he took guidance from a Direct Instruction or Behavior Analysis sponsor but that it might well be disrupted by guidance from one of the more child-centered sponsors.
What Direct Instruction and Behavior Analysis provide are more fully developed instructional systems than teachers normally employ. They provide more systematic ways of determining whether children have the prerequisite skills before a new step in learning is undertaken, more precise ways of monitoring what each child is learning or failing to learn, and more sophisticated instructional moves for dealing with children’s learning needs. Open Education and Responsive Education, on the other hand, because of their avowed opposition to making normative comparisons of students or thinking in terms of deficits, will tend to discourage those activities whereby teachers normally discover when children are not adequately prepared for a new step in learning or when a child has mislearned or failed to learn something. Also, because of their preference for indirect learning activities, these models will tend to make teaching less sharply focused on achieving specific earnings and remedying specific lacks.
Of course, child-centered educators will wish to describe the matter differently, arguing that they do have a well-developed system for promoting learning; but it is a different kind of system pursuing different kinds of goals from those pursued by the direct instructional approaches. They will point out that child-centered teachers devote a great deal of effort to identifying individual pupils’ learning needs and to providing learning experiences to meet these needs; it is just that their efforts are more informal and intuitive, less programmed. Child-centered education, they will argue, is different, not inferior.
One is inclined automatically to assent to this live-and-let-live assessment, which relegates the differences between educational methods to the realm of personal values and ideology. But surely the Follow Through experiment and any comparative evaluation will have been in vain if we take this easy way out of the dilemma of educating disadvantaged children.
This easy way of avoiding confrontation between the two approaches can be opposed on both empirical and theoretical grounds. Empirically, child-centered approaches have been unable to demonstrate any off-setting advantages to compensate for their poor showing in teaching the three R’s. House et al (1978a) have argued that the selection of measures used in the Follow Through evaluation did not give child-centered approaches adequate opportunity to demonstrate their effects. This may be true to a degree, but it is certainly not true that child-centered approaches had no opportunity to demonstrate effects relevant to their purposes. One had better not be a perfectionist when it comes to educational evaluation. No measure is perfectly correlated to one’s objectives. The most one can hope for is a substantial correlation between obtained scores on the actual measures and true scores on the ideally appropriate measures that one wishes existed but do not.
When child-centered educators purport to increase the self-esteem of disadvantaged children and yet fail to show evidence of this on the Coopersmith Self-Concept Inventory, we may ask what real and substantial changes in self-esteem would one expect to occur that would not be reflected in changes on the Coopersmith? Similarly for reasoning and problem-solving. If no evidence of effect shows on a test of non-verbal reasoning, or a reading comprehension test loaded with inferential questions, or on a mathematical problem solving test, we must ask why not? What kinds of real, fundamental improvements in logical reasoning abilities would fail to be reflected in any of these tests?
If these remarks are harsh, it is only because we believe that the question of how best to educate disadvantaged children is sufficiently serious that a policy of live-and-let-live needs to be replaced by a policy of put-up-or-shut-up. Certainly the cause of educational betterment is not advanced by continual appeal to nonexistent measures having zero or negative correlations with existing instruments purporting to measure the same thing. Among the numerous faults that we have found with the House committee’s report, their use of this appeal is the only one that deserves the label of sophistry.
Critique of the Child-centered Approach
What follows is an attempt at a constructive assessment of the child-centered approach as embodied in the Open Education and Responsive Education models. By constructive we mean that we take seriously the goals of these models and that our interest is in realizing the goals rather than in scrapping them in favor of others. These remarks are by way of preface to the following observation: child-centered approaches have evolved sophisticated ways of managing informal educational activities but they have remained at a primitive level in the design of means to achieve learning objectives.
We are here distinguishing between two levels at which a system of teaching may be examined. At the management level, an open classroom and a classroom running according to a token economy, for example, are radically different, and while there is much to dispute in comparing them, it is at least clear that both represent highly evolved systems. When we consider the instructional design level, however, the difference is more one-sided. Child-centered approaches rely almost exclusively on a form of instruction that instructionally-oriented approaches use only when nothing better can be found.
This primitive form of instruction may be called relevant activity. Relevant activity is what teachers must resort to when there is no available way to teach children how to do something, no set of learning activities that clearly converge on an objective. This is the case, for instance, with reading comprehension. Although there are some promising beginnings, there is as yet no adequate “how-to-do-it” scheme for reading comprehension. Accordingly, the best that can be done is to engage students in activities relevant to reading comprehension-for instance, reading selections and answering questions about the selections. Such activities are relevant in that they entail reading comprehension, but they cannot be said to teach reading comprehension.
For many other areas of instruction, however, more sophisticated means have been developed. There are, for instance, ways of teaching children how to decode in reading and how to handle equalities and inequalities in arithmetic (Engelmann, Ref. Note 2). The instructional approaches used in Direct Instruction and Behavior Analysis reflect years of analysis and experimentation devoted to finding ways of going beyond relevant activity to forms of instruction that get more directly at cognitive skills and strategies. This effort has been successful in some areas, not so successful in others, but the effort goes on. Meanwhile, child-centered approaches have tended to fixate on the primitive relevant activities form of instruction for all their instructional objectives.
The contrast of sophistication in management and naiveté in instruction is visible in any well-run open classroom. The behavior that meets the eye is instantly appealing-children quietly absorbed in planning, studying, experimenting, making things-and one has to marvel at the skill and planning that have achieved such a blend of freedom and order. But look at the learning activities themselves and one sees a hodge-podge of the promising and the pointless, of the excessively repetitious and the excessively varied, of tasks that require more thinking than the children are capable of and tasks that have been cleverly designed to require no mental effort at all (like exercise sheets in which all the problems on the page have the same answer). The scatteredness is often appalling. There is a little bit of phonics here and a little bit of phonics there, but never a sufficiently coherent sequence to enable a kid to learn bow to use this valuable tool. Materials have been chosen for sensorial appeal or suitability to the system of management. There is a predilection for cute ideas. The conceptual analysis of learning problems tends to be vague and irrelevant, big on name-dropping and low on incisiveness.
There does not appear to be any intrinsic reason why child-centered educators should have to remain committed to primitive instructional approaches. So far, child-centered educators have been able to gain reassurance from the fact that for the objectives they emphasize-objectives in comprehension, thinking, and feeling-their approaches are no more ineffective than anyone else’s. But even this defense may be crumbling. Instructional designers, having achieved what appears to be substantial success in improving the teaching of decoding in reading, basic mathematical concepts and operations, spelling, and written English syntax, are now turning more of their attention to the kinds of goals emphasized by child-centered educators. Unless thinkers and experimenters committed to child-centered education become more sophisticated about instruction and start devoting more attention to designing learning activities that actually converge on objectives, they are in danger of becoming completely discredited. That would be too bad. Child-centered educators have evolved a style of school life that has much in its favor. Until they develop an effective pedagogy to go with it, however, it does not appear to be an acceptable way of teaching disadvantaged children.
*Graphs and tables in this article could not be reproduced clearly in electronic format.
1. Reduced analyses were performed, dropping TEEM and Cognitive Curriculum from the analysis. These were the two most unstable models in the sense of shifting most in relative performance depending on the choice of covariates. Moreover, Cognitive Curriculum had deviant relations between criteria and covariates, showing for instance negative relationships between achievement and SES. The only effect of removing these models, however, was to increase the number of significant differences between the two top scoring models and the other models.
2. Examined closely, the House et al statement is a bit slippery. Since the MAT is a norm-referenced, (not a criterion-referenced) test, it is of course “reckless” to infer any particular attainments at all from test scores. All we know is how a person or group performs in comparison to others. If, for example, the criterion for “ability to write a story” is set high enough, it would be reckless to suppose that any third-grader had attained it.
3. The obvious targets for the charge of emphasizing rote learning are Direct Instruction and Behavior Analysis. However, the Direct Instruction sponsors explicitly reject rote memorization (Bock, Stebbins, & Proper, 1977, p. 65) and the Behavior Analysis model description makes no mention of it. House, Glass, McLean, and Walker seem to have fallen into the common fallacy here of equating direct instruction with rote learning. If they are like most university professors, they probably rely extensively on direct instruction themselves and yet would be offended by the suggestion that this means they teach by rote.
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2. Engelmann, S. Direct Instruction. Seminar presentation. AERA, Toronto, March, 1978.
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Stephens, J. (1967). The process of schooling. New York: Holt, Rinehart & Winston.
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