example of comparative study research

On Evaluating Curricular Effectiveness: Judging the Quality of K-12 Mathematics Evaluations (2004)

Chapter: 5 comparative studies, 5 comparative studies.

It is deceptively simple to imagine that a curriculum’s effectiveness could be easily determined by a single well-designed study. Such a study would randomly assign students to two treatment groups, one using the experimental materials and the other using a widely established comparative program. The students would be taught the entire curriculum, and a test administered at the end of instruction would provide unequivocal results that would permit one to identify the more effective treatment.

The truth is that conducting definitive comparative studies is not simple, and many factors make such an approach difficult. Student placement and curricular choice are decisions that involve multiple groups of decision makers, accrue over time, and are subject to day-to-day conditions of instability, including student mobility, parent preference, teacher assignment, administrator and school board decisions, and the impact of standardized testing. This complex set of institutional policies, school contexts, and individual personalities makes comparative studies, even quasi-experimental approaches, challenging, and thus demands an honest and feasible assessment of what can be expected of evaluation studies (Usiskin, 1997; Kilpatrick, 2002; Schoenfeld, 2002; Shafer, in press).

Comparative evaluation study is an evolving methodology, and our purpose in conducting this review was to evaluate and learn from the efforts undertaken so far and advise on future efforts. We stipulated the use of comparative studies as follows:

A comparative study was defined as a study in which two (or more) curricular treatments were investigated over a substantial period of time (at least one semester, and more typically an entire school year) and a comparison of various curricular outcomes was examined using statistical tests. A statistical test was required to ensure the robustness of the results relative to the study’s design.

We read and reviewed a set of 95 comparative studies. In this report we describe that database, analyze its results, and draw conclusions about the quality of the evaluation database both as a whole and separated into evaluations supported by the National Science Foundation and commercially generated evaluations. In addition to describing and analyzing this database, we also provide advice to those who might wish to fund or conduct future comparative evaluations of mathematics curricular effectiveness. We have concluded that the process of conducting such evaluations is in its adolescence and could benefit from careful synthesis and advice in order to increase its rigor, feasibility, and credibility. In addition, we took an interdisciplinary approach to the task, noting that various committee members brought different expertise and priorities to the consideration of what constitutes the most essential qualities of rigorous and valid experimental or quasi-experimental design in evaluation. This interdisciplinary approach has led to some interesting observations and innovations in our methodology of evaluation study review.

This chapter is organized as follows:

Study counts disaggregated by program and program type.

Seven critical decision points and identification of at least minimally methodologically adequate studies.

Definition and illustration of each decision point.

A summary of results by student achievement in relation to program types (NSF-supported, University of Chicago School Mathematics Project (UCSMP), and commercially generated) in relation to their reported outcome measures.

A list of alternative hypotheses on effectiveness.

Filters based on the critical decision points.

An analysis of results by subpopulations.

An analysis of results by content strand.

An analysis of interactions among content, equity, and grade levels.

Discussion and summary statements.

In this report, we describe our methodology for review and synthesis so that others might scrutinize our approach and offer criticism on the basis of

our methodology and its connection to the results stated and conclusions drawn. In the spirit of scientific, fair, and open investigation, we welcome others to undertake similar or contrasting approaches and compare and discuss the results. Our work was limited by the short timeline set by the funding agencies resulting from the urgency of the task. Although we made multiple efforts to collect comparative studies, we apologize to any curriculum evaluators if comparative studies were unintentionally omitted from our database.

Of these 95 comparative studies, 65 were studies of NSF-supported curricula, 27 were studies of commercially generated materials, and 3 included two curricula each from one of these two categories. To avoid the problem of double coding, two studies, White et al. (1995) and Zahrt (2001), were coded within studies of NSF-supported curricula because more of the classes studied used the NSF-supported curriculum. These studies were not used in later analyses because they did not meet the requirements for the at least minimally methodologically adequate studies, as described below. The other, Peters (1992), compared two commercially generated curricula, and was coded in that category under the primary program of focus. Therefore, of the 95 comparative studies, 67 studies were coded as NSF-supported curricula and 28 were coded as commercially generated materials.

The 11 evaluation studies of the UCSMP secondary program that we reviewed, not including White et al. and Zahrt as previously mentioned, benefit from the maturity of the program, while demonstrating an orientation to both establishing effectiveness and improving a product line. For these reasons, at times we will present the summary of UCSMP’s data separately.

The Saxon materials also present a somewhat different profile from the other commercially generated materials because many of the evaluations of these materials were conducted in the 1980s and the materials were originally developed with a rather atypical program theory. Saxon (1981) designed its algebra materials to combine distributed practice with incremental development. We selected the Saxon materials as a middle grades commercially generated program, and limited its review to middle school studies from 1989 onward when the first National Council of Teachers of Mathematics (NCTM) Standards (NCTM, 1989) were released. This eliminated concerns that the materials or the conditions of educational practice have been altered during the intervening time period. The Saxon materials explicitly do not draw from the NCTM Standards nor did they receive support from the NSF; thus they truly represent a commercial venture. As a result, we categorized the Saxon studies within the group of studies of commercial materials.

At times in this report, we describe characteristics of the database by

FIGURE 5-1 The distribution of comparative studies across programs. Programs are coded by grade band: black bars = elementary, white bars = middle grades, and gray bars = secondary. In this figure, there are six studies that involved two programs and one study that involved three programs.

NOTE: Five programs (MathScape, MMAP, MMOW/ARISE, Addison-Wesley, and Harcourt) are not shown above since no comparative studies were reviewed.

particular curricular program evaluations, in which case all 19 programs are listed separately. At other times, when we seek to inform ourselves on policy-related issues of funding and evaluating curricular materials, we use the NSF-supported, commercially generated, and UCSMP distinctions. We remind the reader of the artificial aspects of this distinction because at the present time, 18 of the 19 curricula are published commercially. In order to track the question of historical inception and policy implications, a distinction is drawn between the three categories. Figure 5-1 shows the distribution of comparative studies across the 14 programs.

The first result the committee wishes to report is the uneven distribution of studies across the curricula programs. There were 67 coded studies of the NSF curricula, 11 studies of UCSMP, and 17 studies of the commercial publishers. The 14 evaluation studies conducted on the Saxon materials compose the bulk of these 17-non-UCSMP and non-NSF-supported curricular evaluation studies. As these results suggest, we know more about the

evaluations of the NSF-supported curricula and UCSMP than about the evaluations of the commercial programs. We suggest that three factors account for this uneven distribution of studies. First, evaluations have been funded by the NSF both as a part of the original call, and as follow-up to the work in the case of three supplemental awards to two of the curricula programs. Second, most NSF-supported programs and UCSMP were developed at university sites where there is access to the resources of graduate students and research staff. Finally, there was some reported reluctance on the part of commercial companies to release studies that could affect perceptions of competitive advantage. As Figure 5-1 shows, there were quite a few comparative studies of Everyday Mathematics (EM), Connected Mathematics Project (CMP), Contemporary Mathematics in Context (Core-Plus Mathematics Project [CPMP]), Interactive Mathematics Program (IMP), UCSMP, and Saxon.

In the programs with many studies, we note that a significant number of studies were generated by a core set of authors. In some cases, the evaluation reports follow a relatively uniform structure applied to single schools, generating multiple studies or following cohorts over years. Others use a standardized evaluation approach to evaluate sequential courses. Any reports duplicating exactly the same sample, outcome measures, or forms of analysis were eliminated. For example, one study of Mathematics Trailblazers (Carter et al., 2002) reanalyzed the data from the larger ARC Implementation Center study (Sconiers et al., 2002), so it was not included separately. Synthesis studies referencing a variety of evaluation reports are summarized in Chapter 6 , but relevant individual studies that were referenced in them were sought out and included in this comparative review.

Other less formal comparative studies are conducted regularly at the school or district level, but such studies were not included in this review unless we could obtain formal reports of their results, and the studies met the criteria outlined for inclusion in our database. In our conclusions, we address the issue of how to collect such data more systematically at the district or state level in order to subject the data to the standards of scholarly peer review and make it more systematically and fairly a part of the national database on curricular effectiveness.

A standard for evaluation of any social program requires that an impact assessment is warranted only if two conditions are met: (1) the curricular program is clearly specified, and (2) the intervention is well implemented. Absent this assurance, one must have a means of ensuring or measuring treatment integrity in order to make causal inferences. Rossi et al. (1999, p. 238) warned that:

two prerequisites [must exist] for assessing the impact of an intervention. First, the program’s objectives must be sufficiently well articulated to make

it possible to specify credible measures of the expected outcomes, or the evaluator must be able to establish such a set of measurable outcomes. Second, the intervention should be sufficiently well implemented that there is no question that its critical elements have been delivered to appropriate targets. It would be a waste of time, effort, and resources to attempt to estimate the impact of a program that lacks measurable outcomes or that has not been properly implemented. An important implication of this last consideration is that interventions should be evaluated for impact only when they have been in place long enough to have ironed out implementation problems.

These same conditions apply to evaluation of mathematics curricula. The comparative studies in this report varied in the quality of documentation of these two conditions; however, all addressed them to some degree or another. Initially by reviewing the studies, we were able to identify one general design template, which consisted of seven critical decision points and determined that it could be used to develop a framework for conducting our meta-analysis. The seven critical decision points we identified initially were:

Choice of type of design: experimental or quasi-experimental;

For those studies that do not use random assignment: what methods of establishing comparability of groups were built into the design—this includes student characteristics, teacher characteristics, and the extent to which professional development was involved as part of the definition of a curriculum;

Definition of the appropriate unit of analysis (students, classes, teachers, schools, or districts);

Inclusion of an examination of implementation components;

Definition of the outcome measures and disaggregated results by program;

The choice of statistical tests, including statistical significance levels and effect size; and

Recognition of limitations to generalizability resulting from design choices.

These are critical decisions that affect the quality of an evaluation. We further identified a subset of these evaluation studies that met a set of minimum conditions that we termed at least minimally methodologically adequate studies. Such studies are those with the greatest likelihood of shedding light on the effectiveness of these programs. To be classified as at least minimally methodologically adequate, and therefore to be considered for further analysis, each evaluation study was required to:

Include quantifiably measurable outcomes such as test scores, responses to specified cognitive tasks of mathematical reasoning, performance evaluations, grades, and subsequent course taking; and

Provide adequate information to judge the comparability of samples. In addition, a study must have included at least one of the following additional design elements:

A report of implementation fidelity or professional development activity;

Results disaggregated by content strands or by performance by student subgroups; and/or

Multiple outcome measures or precise theoretical analysis of a measured construct, such as number sense, proof, or proportional reasoning.

Using this rubric, the committee identified a subset of 63 comparative studies to classify as at least minimally methodologically adequate and to analyze in depth to inform the conduct of future evaluations. There are those who would argue that any threat to the validity of a study discredits the findings, thus claiming that until we know everything, we know nothing. Others would claim that from the myriad of studies, examining patterns of effects and patterns of variation, one can learn a great deal, perhaps tentatively, about programs and their possible effects. More importantly, we can learn about methodologies and how to concentrate and focus to increase the likelihood of learning more quickly. As Lipsey (1997, p. 22) wrote:

In the long run, our most useful and informative contribution to program managers and policy makers and even to the evaluation profession itself may be the consolidation of our piecemeal knowledge into broader pictures of the program and policy spaces at issue, rather than individual studies of particular programs.

We do not wish to imply that we devalue studies of student affect or conceptions of mathematics, but decided that unless these indicators were connected to direct indicators of student learning, we would eliminate them from further study. As a result of this sorting, we eliminated 19 studies of NSF-supported curricula and 13 studies of commercially generated curricula. Of these, 4 were eliminated for their sole focus on affect or conceptions, 3 were eliminated for their comparative focus on outcomes other than achievement, such as teacher-related variables, and 19 were eliminated for their failure to meet the minimum additional characteristics specified in the criteria above. In addition, six others were excluded from the studies of commercial materials because they were not conducted within the grade-

level band specified by the committee for the selection of that program. From this point onward, all references can be assumed to refer to at least minimally methodologically adequate unless a study is referenced for illustration, in which case we label it with “EX” to indicate that it is excluded in the summary analyses. Studies labeled “EX” are occasionally referenced because they can provide useful information on certain aspects of curricular evaluation, but not on the overall effectiveness.

The at least minimally methodologically adequate studies reported on a variety of grade levels. Figure 5-2 shows the different grade levels of the studies. At times, the choice of grade levels was dictated by the years in which high-stakes tests were given. Most of the studies reported on multiple grade levels, as shown in Figure 5-2 .

Using the seven critical design elements of at least minimally methodologically adequate studies as a design template, we describe the overall database and discuss the array of choices on critical decision points with examples. Following that, we report on the results on the at least minimally methodologically adequate studies by program type. To do so, the results of each study were coded as either statistically significant or not. Those studies

FIGURE 5-2 Single-grade studies by grade and multigrade studies by grade band.

that contained statistically significant results were assigned a percentage of outcomes that are positive (in favor of the treatment curriculum) based on the number of statistically significant comparisons reported relative to the total number of comparisons reported, and a percentage of outcomes that are negative (in favor of the comparative curriculum). The remaining were coded as the percentage of outcomes that are non significant. Then, using seven critical decision points as filters, we identified and examined more closely sets of studies that exhibited the strongest designs, and would therefore be most likely to increase our confidence in the validity of the evaluation. In this last section, we consider alternative hypotheses that could explain the results.

The committee emphasizes that we did not directly evaluate the materials. We present no analysis of results aggregated across studies by naming individual curricular programs because we did not consider the magnitude or rigor of the database for individual programs substantial enough to do so. Nevertheless, there are studies that provide compelling data concerning the effectiveness of the program in a particular context. Furthermore, we do report on individual studies and their results to highlight issues of approach and methodology and to remain within our primary charge, which was to evaluate the evaluations, we do not summarize results of the individual programs.

DESCRIPTION OF COMPARATIVE STUDIES DATABASE ON CRITICAL DECISION POINTS

An experimental or quasi-experimental design.

We separated the studies into experimental and quasiexperimental, and found that 100 percent of the studies were quasiexperimental (Campbell and Stanley, 1966; Cook and Campbell, 1979; and Rossi et al., 1999). 1 Within the quasi-experimental studies, we identified three subcategories of comparative study. In the first case, we identified a study as cross-curricular comparative if it compared the results of curriculum A with curriculum B. A few studies in this category also compared two samples within the curriculum to each other and specified different conditions such as high and low implementation quality.

A second category of a quasi-experimental study involved comparisons that could shed light on effectiveness involving time series studies. These studies compared the performance of a sample of students in a curriculum

FIGURE 5-3 The number of comparative studies in each category.

under investigation across time, such as in a longitudinal study of the same students over time. A third category of comparative study involved a comparison to some form of externally normed results, such as populations taking state, national, or international tests or prior research assessment from a published study or studies. We categorized these studies and divided them into NSF, UCSMP, and commercial and labeled them by the categories above ( Figure 5-3 ).

In nearly all studies in the comparative group, the titles of experimental curricula were explicitly identified. The only exception to this was the ARC Implementation Center study (Sconiers et al., 2002), where three NSF-supported elementary curricula were examined, but in the results, their effects were pooled. In contrast, in the majority of the cases, the comparison curriculum is referred to simply as “traditional.” In only 22 cases were comparisons made between two identified curricula. Many others surveyed the array of curricula at comparison schools and reported on the most frequently used, but did not identify a single curriculum. This design strategy is used often because other factors were used in selecting comparison groups, and the additional requirement of a single identified curriculum in

these sites would often make it difficult to match. Studies were categorized into specified (including a single or multiple identified curricula) and nonspecified curricula. In the 63 studies, the central group was compared to an NSF-supported curriculum (1), an unnamed traditional curriculum (41), a named traditional curriculum (19), and one of the six commercial curricula (2). To our knowledge, any systematic impact of such a decision on results has not been studied, but we express concern that when a specified curriculum is compared to an unspecified content which is a set of many informal curriculum, the comparison may favor the coherency and consistency of the single curricula, and we consider this possibility subsequently under alternative hypotheses. We believe that a quality study should at least report the array of curricula that comprise the comparative group and include a measure of the frequency of use of each, but a well-defined alternative is more desirable.

If a study was both longitudinal and comparative, then it was coded as comparative. When studies only examined performances of a group over time, such as in some longitudinal studies, it was coded as quasi-experimental normed. In longitudinal studies, the problems created by student mobility were evident. In one study, Carroll (2001), a five-year longitudinal study of Everyday Mathematics, the sample size began with 500 students, 24 classrooms, and 11 schools. By 2nd grade, the longitudinal sample was 343. By 3rd grade, the number of classes increased to 29 while the number of original students decreased to 236 students. At the completion of the study, approximately 170 of the original students were still in the sample. This high rate of attrition from the study suggests that mobility is a major challenge in curricular evaluation, and that the effects of curricular change on mobile students needs to be studied as a potential threat to the validity of the comparison. It is also a challenge in curriculum implementation because students coming into a program do not experience its cumulative, developmental effect.

Longitudinal studies also have unique challenges associated with outcome measures, a study by Romberg et al. (in press) (EX) discussed one approach to this problem. In this study, an external assessment system and a problem-solving assessment system were used. In the External Assessment System, items from the National Assessment of Educational Progress (NAEP) and Third International Mathematics and Science Survey (TIMSS) were balanced across four strands (number, geometry, algebra, probability and statistics), and 20 items of moderate difficulty, called anchor items, were repeated on each grade-specific assessment (p. 8). Because the analyses of the results are currently under way, the evaluators could not provide us with final results of this study, so it is coded as EX.

However, such longitudinal studies can provide substantial evidence of the effects of a curricular program because they may be more sensitive to an

TABLE 5-1 Scores in Percentage Correct by Everyday Mathematics Students and Various Comparison Groups Over a Five-Year Longitudinal Study

accumulation of modest effects and/or can reveal whether the rates of learning change over time within curricular change.

The longitudinal study by Carroll (2001) showed that the effects of curricula may often accrue over time, but measurements of achievement present challenges to drawing such conclusions as the content and grade level change. A variety of measures were used over time to demonstrate growth in relation to comparison groups. The author chose a set of measures used previously in studies involving two Asian samples and an American sample to provide a contrast to the students in EM over time. For 3rd and 4th grades, where the data from the comparison group were not available, the authors selected items from the NAEP to bridge the gap. Table 5-1 summarizes the scores of the different comparative groups over five years. Scores are reported as the mean percentage correct for a series of tests on number computation, number concepts and applications, geometry, measurement, and data analysis.

It is difficult to compare performances on different tests over different groups over time against a single longitudinal group from EM, and it is not possible to determine whether the students’ performance is increasing or whether the changes in the tests at each grade level are producing the results; thus the results from longitudinal studies lacking a control group or use of sophisticated methodological analysis may be suspect and should be interpreted with caution.

In the Hirsch and Schoen (2002) study, based on a sample of 1,457 students, scores on Ability to Do Quantitative Thinking (ITED-Q) a subset of the Iowa Tests of Education Development, students in Core-Plus showed increasing performance over national norms over the three-year time period. The authors describe the content of the ITED-Q test and point out

that “although very little symbolic algebra is required, the ITED-Q is quite demanding for the full range of high school students” (p. 3). They further point out that “[t]his 3-year pattern is consistent, on average, in rural, urban, and suburban schools, for males and females, for various minority groups, and for students for whom English was not their first language” (p. 4). In this case, one sees that studies over time are important as results over shorter periods may mask cumulative effects of consistent and coherent treatments and such studies could also show increases that do not persist when subject to longer trajectories. One approach to longitudinal studies was used by Webb and Dowling in their studies of the Interactive Mathematics Program (Webb and Dowling, 1995a, 1995b, 1995c). These researchers conducted transcript analyses as a means to examine student persistence and success in subsequent course taking.

The third category of quasi-experimental comparative studies measured student outcomes on a particular curricular program and simply compared them to performance on national tests or international tests. When these tests were of good quality and were representative of a genuine sample of a relevant population, such as NAEP reports or TIMSS results, the reports often provided one a reasonable indicator of the effects of the program if combined with a careful description of the sample. Also, sometimes the national tests or state tests used were norm-referenced tests producing national percentiles or grade-level equivalents. The normed studies were considered of weaker quality in establishing effectiveness, but were still considered valid as examples of comparing samples to populations.

For Studies That Do Not Use Random Assignment: What Methods of Establishing Comparability Across Groups Were Built into the Design

The most fundamental question in an evaluation study is whether the treatment has had an effect on the chosen criterion variable. In our context, the treatment is the curriculum materials, and in some cases, related professional development, and the outcome of interest is academic learning. To establish if there is a treatment effect, one must logically rule out as many other explanations as possible for the differences in the outcome variable. There is a long tradition on how this is best done, and the principle from a design point of view is to assure that there are no differences between the treatment conditions (especially in these evaluations, often there are only the new curriculum materials to be evaluated and a control group) either at the outset of the study or during the conduct of the study.

To ensure the first condition, the ideal procedure is the random assignment of the appropriate units to the treatment conditions. The second condition requires that the treatment is administered reliably during the length of the study, and is assured through the careful observation and

control of the situation. Without randomization, there are a host of possible confounding variables that could differ among the treatment conditions and that are related themselves to the outcome variables. Put another way, the treatment effect is a parameter that the study is set up to estimate. Statistically, an estimate that is unbiased is desired. The goal is that its expected value over repeated samplings is equal to the true value of the parameter. Without randomization at the onset of a study, there is no way to assure this property of unbiasness. The variables that differ across treatment conditions and are related to the outcomes are confounding variables, which bias the estimation process.

Only one study we reviewed, Peters (1992), used randomization in the assignment of students to treatments, but that occurred because the study was limited to one teacher teaching two sections and included substantial qualitative methods, so we coded it as quasi-experimental. Others report partially assigning teachers randomly to treatment conditions (Thompson, et al., 2001; Thompson et al., 2003). Two primary reasons seem to account for a lack of use of pure experimental design. To justify the conduct and expense of a randomized field trial, the program must be described adequately and there must be relative assurance that its implementation has occurred over the duration of the experiment (Peterson et al., 1999). Additionally, one must be sure that the outcome measures are appropriate for the range of performances in the groups and valid relative to the curricula under investigation. Seldom can such conditions be assured for all students and teachers and over the duration of a year or more.

A second reason is that random assignment of classrooms to curricular treatment groups typically is not permitted or encouraged under normal school conditions. As one evaluator wrote, “Building or district administrators typically identified teachers who would be in the study and in only a few cases was random assignment of teachers to UCSMP Algebra or comparison classes possible. School scheduling and teacher preference were more important factors to administrators and at the risk of losing potential sites, we did not insist on randomization” (Mathison et al., 1989, p. 11).

The Joint Committee on Standards for Educational Evaluation (1994, p. 165) committee of evaluations recognized the likelihood of limitations on randomization, writing:

The groups being compared are seldom formed by random assignment. Rather, they tend to be natural groupings that are likely to differ in various ways. Analytical methods may be used to adjust for these initial differences, but these methods are based upon a number of assumptions. As it is often difficult to check such assumptions, it is advisable, when time and resources permit, to use several different methods of analysis to determine whether a replicable pattern of results is obtained.

Does the dearth of pure experimentation render the results of the studies reviewed worthless? Bias is not an “either-or” proposition, but it is a quantity of varying degrees. Through careful measurement of the most salient potential confounding variables, precise theoretical description of constructs, and use of these methods of statistical analysis, it is possible to reduce the amount of bias in the estimated treatment effect. Identification of the most likely confounding variables and their measurement and subsequent adjustments can greatly reduce bias and help estimate an effect that is likely to be more reflective of the true value. The theoretical fully specified model is an alternative to randomization by including relevant variables and thus allowing the unbiased estimation of the parameter. The only problem is realizing when the model is fully specified.

We recognized that we can never have enough knowledge to assure a fully specified model, especially in the complex and unstable conditions of schools. However, a key issue in determining the degree of confidence we have in these evaluations is to examine how they have identified, measured, or controlled for such confounding variables. In the next sections, we report on the methods of the evaluators in identifying and adjusting for such potential confounding variables.

One method to eliminate confounding variables is to examine the extent to which the samples investigated are equated either by sample selection or by methods of statistical adjustments. For individual students, there is a large literature suggesting the importance of social class to achievement. In addition, prior achievement of students must be considered. In the comparative studies, investigators first identified participation of districts, schools, or classes that could provide sufficient duration of use of curricular materials (typically two years or more), availability of target classes, or adequate levels of use of program materials. Establishing comparability was a secondary concern.

These two major factors were generally used in establishing the comparability of the sample:

Student population characteristics, such as demographic characteristics of students in terms of race/ethnicity, economic levels, or location type (urban, suburban, or rural).

Performance-level characteristics such as performance on prior tests, pretest performance, percentage passing standardized tests, or related measures (e.g., problem solving, reading).

In general, four methods of comparing groups were used in the studies we examined, and they permit different degrees of confidence in their results. In the first type, a matching class, school, or district was identified.

Studies were coded as this type if specified characteristics were used to select the schools systematically. In some of these studies, the methodology was relatively complex as correlates of performance on the outcome measures were found empirically and matches were created on that basis (Schneider, 2000; Riordan and Noyce, 2001; and Sconiers et al., 2002). For example, in the Sconiers et al. study, where the total sample of more than 100,000 students was drawn from five states and three elementary curricula are reviewed (Everyday Mathematics, Math Trailblazers [MT], and Investigations [IN], a highly systematic method was developed. After defining eligibility as a “reform school,” evaluators conducted separate regression analyses for the five states at each tested grade level to identify the strongest predictors of average school mathematics score. They reported, “reading score and low-income variables … consistently accounted for the greatest percentage of total variance. These variables were given the greatest weight in the matching process. Other variables—such as percent white, school mobility rate, and percent with limited English proficiency (LEP)—accounted for little of the total variance but were typically significant. These variables were given less weight in the matching process” (Sconiers et al., 2002, p. 10). To further provide a fair and complete comparison, adjustments were made based on regression analysis of the scores to minimize bias prior to calculating the difference in scores and reporting effect sizes. In their results the evaluators report, “The combined state-grade effect sizes for math and total are virtually identical and correspond to a percentile change of about 4 percent favoring the reform students” (p. 12).

A second type of matching procedure was used in the UCSMP evaluations. For example, in an evaluation centered on geometry learning, evaluators advertised in NCTM and UCSMP publications, and set conditions for participation from schools using their program in terms of length of use and grade level. After selecting schools with heterogeneous grouping and no tracking, the researchers used a match-pair design where they selected classes from the same school on the basis of mathematics ability. They used a pretest to determine this, and because the pretest consisted of two parts, they adjusted their significance level using the Bonferroni method. 2 Pairs were discarded if the differences in means and variance were significant for all students or for those students completing all measures, or if class sizes became too variable. In the algebra study, there were 20 pairs as a result of the matching, and because they were comparing three experimental conditions—first edition, second edition, and comparison classes—in the com-

parison study relevant to this review, their matching procedure identified 8 pairs. When possible, teachers were assigned randomly to treatment conditions. Most results are presented with the eight identified pairs and an accumulated set of means. The outcomes of this particular study are described below in a discussion of outcome measures (Thompson et al., 2003).

A third method was to measure factors such as prior performance or socio-economic status (SES) based on pretesting, and then to use analysis of covariance or multiple regression in the subsequent analysis to factor in the variance associated with these factors. These studies were coded as “control.” A number of studies of the Saxon curricula used this method. For example, Rentschler (1995) conducted a study of Saxon 76 compared to Silver Burdett with 7th graders in West Virginia. He reported that the groups differed significantly in that the control classes had 65 percent of the students on free and reduced-price lunch programs compared to 55 percent in the experimental conditions. He used scores on California Test of Basic Skills mathematics computation and mathematics concepts and applications as his pretest scores and found significant differences in favor of the experimental group. His posttest scores showed the Saxon experimental group outperformed the control group on both computation and concepts and applications. Using analysis of covariance, the computation difference in favor of the experimental group was statistically significant; however, the difference in concepts and applications was adjusted to show no significant difference at the p < .05 level.

A fourth method was noted in studies that used less rigorous methods of selection of sample and comparison of prior achievement or similar demographics. These studies were coded as “compare.” Typically, there was no explicit procedure to decide if the comparison was good enough. In some of the studies, it appeared that the comparison was not used as a means of selection, but rather as a more informal device to convince the reader of the plausibility of the equivalence of the groups. Clearly, the studies that used a more precise method of selection were more likely to produce results on which one’s confidence in the conclusions is greater.

Definition of Unit of Analysis

A major decision in forming an evaluation design is the unit of analysis. The unit of selection or randomization used to assign elements to treatment and control groups is closely linked to the unit of analysis. As noted in the National Research Council (NRC) report (1992, p. 21):

If one carries out the assignment of treatments at the level of schools, then that is the level that can be justified for causal analysis. To analyze the results at the student level is to introduce a new, nonrandomized level into

the study, and it raises the same issues as does the nonrandomized observational study…. The implications … are twofold. First, it is advisable to use randomization at the level at which units are most naturally manipulated. Second, when the unit of observation is at a “lower” level of aggregation than the unit of randomization, then for many purposes the data need to be aggregated in some appropriate fashion to provide a measure that can be analyzed at the level of assignment. Such aggregation may be as simple as a summary statistic or as complex as a context-specific model for association among lower-level observations.

In many studies, inadequate attention was paid to the fact that the unit of selection would later become the unit of analysis. The unit of analysis, for most curriculum evaluators, needs to be at least the classroom, if not the school or even the district. The units must be independently responding units because instruction is a group process. Students are not independent, the classroom—even if the teachers work together in a school on instruction—is not entirely independent, so the school is the unit. Care needed to be taken to ensure that an adequate numbers of units would be available to have sufficient statistical power to detect important differences.

A curriculum is experienced by students in a group, and this implies that individual student responses and what they learn are correlated. As a result, the appropriate unit of assignment and analysis must at least be defined at the classroom or teacher level. Other researchers (Bryk et al., 1993) suggest that the unit might be better selected at an even higher level of aggregation. The school itself provides a culture in which the curriculum is enacted as it is influenced by the policies and assignments of the principal, by the professional interactions and governance exhibited by the teachers as a group, and by the community in which the school resides. This would imply that the school might be the appropriate unit of analysis. Even further, to the extent that such decisions about curriculum are made at the district level and supported through resources and professional development at that level, the appropriate unit could arguably be the district. On a more practical level, we found that arguments can be made for a variety of decisions on the selection of units, and what is most essential is to make a clear argument for one’s choice, to use the same unit in the analysis as in the sample selection process, and to recognize the potential limits to generalization that result from one’s decisions.

We would argue in all cases that reports of how sites are selected must be explicit in the evaluation report. For example, one set of evaluation studies selected sites by advertisements in a journal distributed by the program and in NCTM journals (UCSMP) (Thompson et al., 2001; Thompson et al., 2003). The samples in their studies tended to be affluent suburban populations and predominantly white populations. Other conditions of inclusion, such as frequency of use also might have influenced this outcome,

but it is important that over a set of studies on effectiveness, all populations of students be adequately sampled. When a study is not randomized, adjustments for these confounding variables should be included. In our analysis of equity, we report on the concerns about representativeness of the overall samples and their impact on the generalizability of the results.

Implementation Components

The complexity of doing research on curricular materials introduces a number of possible confounding variables. Due to the documented complexity of curricular implementation, most comparative study evaluators attempt to monitor implementation in some fashion. A valuable outcome of a well-conducted evaluation is to determine not only if the experimental curriculum could ideally have a positive impact on learning, but whether it can survive or thrive in the conditions of schooling that are so variable across sites. It is essential to know what the treatment was, whether it occurred, and if so, to what degree of intensity, fidelity, duration, and quality. In our model in Chapter 3 , these factors were referred to as “implementation components.” Measuring implementation can be costly for large-scale comparative studies; however, many researchers have shown that variation in implementation is a key factor in determining effectiveness. In coding the comparative studies, we identified three types of components that help to document the character of the treatment: implementation fidelity, professional development treatments, and attention to teacher effects.

Implementation Fidelity

Implementation fidelity is a measure of the basic extent of use of the curricular materials. It does not address issues of instructional quality. In some studies, implementation fidelity is synonymous with “opportunity to learn.” In examining implementation fidelity, a variety of data were reported, including, most frequently, the extent of coverage of the curricular material, the consistency of the instructional approach to content in relation to the program’s theory, reports of pedagogical techniques, and the length of use of the curricula at the sample sites. Other less frequently used approaches documented the calendar of curricular coverage, requested teacher feedback by textbook chapter, conducted student surveys, and gauged homework policies, use of technology, and other particular program elements. Interviews with teachers and students, classroom surveys, and observations were the most frequently used data-gathering techniques. Classroom observations were conducted infrequently in these studies, except in cases when comparative studies were combined with case studies, typically with small numbers of schools and classes where observations

were conducted for long or frequent time periods. In our analysis, we coded only the presence or absence of one or more of these methods.

If the extent of implementation was used in interpreting the results, then we classified the study as having adjusted for implementation differences. Across all 63 at least minimally methodologically adequate studies, 44 percent reported some type of implementation fidelity measure, 3 percent reported and adjusted for it in interpreting their outcome measures, and 53 percent recorded no information on this issue. Differences among studies, by study type (NSF, UCSMP, and commercially generated), showed variation on this issue, with 46 percent of NSF reporting or adjusting for implementation, 75 percent of UCSMP, and only 11 percent of the other studies of commercial materials doing so. Of the commercial, non-UCSMP studies included, only one reported on implementation. Possibly, the evaluators for the NSF and UCSMP Secondary programs recognized more clearly that their programs demanded significant changes in practice that could affect their outcomes and could pose challenges to the teachers assigned to them.

A study by Abrams (1989) (EX) 3 on the use of Saxon algebra by ninth graders showed that concerns for implementation fidelity extend to all curricula, even those like Saxon whose methods may seem more likely to be consistent with common practice. Abrams wrote, “It was not the intent of this study to determine the effectiveness of the Saxon text when used as Saxon suggests, but rather to determine the effect of the text as it is being used in the classroom situations. However, one aspect of the research was to identify how the text is being taught, and how closely teachers adhere to its content and the recommended presentation” (p. 7). Her findings showed that for the 9 teachers and 300 students, treatment effects favoring the traditional group (using Dolciani’s Algebra I textbook, Houghton Mifflin, 1980) were found on the algebra test, the algebra knowledge/skills subtest, and the problem-solving test for this population of teachers (fixed effect). No differences were found between the groups on an algebra understanding/applications subtest, overall attitude toward mathematics, mathematical self-confidence, anxiety about mathematics, or enjoyment of mathematics. She suggests that the lack of differences might be due to the ways in which teachers supplement materials, change test conditions, emphasize

and deemphasize topics, use their own tests, vary the proportion of time spent on development and practice, use calculators and group work, and basically adapt the materials to their own interpretation and method. Many of these practices conflict directly with the recommendations of the authors of the materials.

A study by Briars and Resnick (2000) (EX) in Pittsburgh schools directly confronted issues relevant to professional development and implementation. Evaluators contrasted the performance of students of teachers with high and low implementation quality, and showed the results on two contrasting outcome measures, Iowa Test of Basic Skills (ITBS) and Balanced Assessment. Strong implementers were defined as those who used all of the EM components and provided student-centered instruction by giving students opportunities to explore mathematical ideas, solve problems, and explain their reasoning. Weak implementers were either not using EM or using it so little that the overall instruction in the classrooms was “hardly distinguishable from traditional mathematics instruction” (p. 8). Assignment was based on observations of student behavior in classes, the presence or absence of manipulatives, teacher questionnaires about the programs, and students’ knowledge of classroom routines associated with the program.

From the identification of strong- and weak-implementing teachers, strong- and weak-implementation schools were identified as those with strong- or weak-implementing teachers in 3rd and 4th grades over two consecutive years. The performance of students with 2 years of EM experience in these settings composed the comparative samples. Three pairs of strong- and weak-implementation schools with similar demographics in terms of free and reduced-price lunch (range 76 to 93 percent), student living with only one parent (range 57 to 82 percent), mobility (range 8 to 16 percent), and ethnicity (range 43 to 98 percent African American) were identified. These students’ 1st-grade ITBS scores indicated similarity in prior performance levels. Finally, evaluators predicted that if the effects were due to the curricular implementation and accompanying professional development, the effects on scores should be seen in 1998, after full implementation. Figure 5-4 shows that on the 1998 New Standards exams, placement in strong- and weak-implementation schools strongly affected students’ scores. Over three years, performance in the district on skills, concepts, and problem solving rose, confirming the evaluator’s predictions.

An article by McCaffrey et al. (2001) examining the interactions among instructional practices, curriculum, and student achievement illustrates the point that distinctions are often inadequately linked to measurement tools in their treatment of the terms traditional and reform teaching. In this study, researchers conducted an exploratory factor analysis that led them to create two scales for instructional practice: Reform Practices and Tradi-

FIGURE 5-4 Percentage of students who met or exceeded the standard. Districtwide grade 4 New Standards Mathematics Reference Examination (NSMRE) performance for 1996, 1997, and 1998 by level of Everyday Mathematics implementation. Percentage of students who achieved the standard. Error bars denote the 99 percent confidence interval for each data point.

SOURCE: Re-created from Briars and Resnick (2000, pp. 19-20).

tional Practices. The reform scale measured the frequency, by means of teacher report, of teacher and student behaviors associated with reform instruction and assessment practices, such as using small-group work, explaining reasoning, representing and using data, writing reflections, or performing tasks in groups. The traditional scale focused on explanations to whole classes, the use of worksheets, practice, and short-answer assessments. There was a –0.32 correlation between scores for integrated curriculum teachers. There was a 0.27 correlation between scores for traditional

curriculum teachers. This shows that it is overly simplistic to think that reform and traditional practices are oppositional. The relationship among a variety of instructional practices is rather more complex as they interact with curriculum and various student populations.

Professional Development

Professional development and teacher effects were separated in our analysis from implementation fidelity. We recognized that professional development could be viewed by the readers of this report in two ways. As indicated in our model, professional development can be considered a program element or component or it can be viewed as part of the implementation process. When viewed as a program element, professional development resources are considered mandatory along with program materials. In relation to evaluation, proponents of considering professional development as a mandatory program element argue that curricular innovations, which involve the introduction of new topics, new types of assessment, or new ways of teaching, must make provision for adequate training, just as with the introduction of any new technology.

For others, the inclusion of professional development in the program elements without a concomitant inclusion of equal amounts of professional development relevant to a comparative treatment interjects a priori disproportionate treatments and biases the results. We hoped for an array of evaluation studies that might shed some empirical light on this dispute, and hence separated professional development from treatment fidelity, coding whether or not studies reported on the amount of professional development provided for the treatment and/or comparison groups. A study was coded as positive if it either reported on the professional development provided on the experimental group or reported the data on both treatments. Across all 63 at least minimally methodologically adequate studies, 27 percent reported some type of professional development measure, 1.5 percent reported and adjusted for it in interpreting their outcome measures, and 71.5 percent recorded no information on the issue.

A study by Collins (2002) (EX) 4 illustrates the critical and controversial role of professional development in evaluation. Collins studied the use of Connected Math over three years, in three middle schools in threat of being classified as low performing in the Massachusetts accountability system. A comparison was made between one school (School A) that engaged

substantively in professional development opportunities accompanying the program and two that did not (Schools B and C). In the CMP school reports (School A) totals between 100 and 136 hours of professional development were recorded for all seven teachers in grades 6 through 8. In School B, 66 hours were reported for two teachers and in School C, 150 hours were reported for eight teachers over three years. Results showed significant differences in the subsequent performance by students at the school with higher participation in professional development (School A) and it became a districtwide top performer; the other two schools remained at risk for low performance. No controls for teacher effects were possible, but the results do suggest the centrality of professional development for successful implementation or possibly suggest that the results were due to professional development rather than curriculum materials. The fact that these two interpretations cannot be separated is a problem when professional development is given to one and not the other. The effect could be due to textbook or professional development or an interaction between the two. Research designs should be adjusted to consider these issues when different conditions of professional development are provided.

Teacher Effects

These studies make it obvious that there are potential confounding factors of teacher effects. Many evaluation studies devoted inadequate attention to the variable of teacher quality. A few studies (Goodrow, 1998; Riordan and Noyce, 2001; Thompson et al., 2001; and Thompson et al., 2003) reported on teacher characteristics such as certification, length of service, experience with curricula, or degrees completed. Those studies that matched classrooms and reported by matched results rather than aggregated results sought ways to acknowledge the large variations among teacher performance and its impact on student outcomes. We coded any effort to report on possible teacher effects as one indicator of quality. Across all 63 at least minimally methodologically adequate studies, 16 percent reported some type of teacher effect measure, 3 percent reported and adjusted for it in interpreting their outcome measures, and 81 percent recorded no information on this issue.

One can see that the potential confounding factors of teacher effects, in terms of the provision of professional development or the measure of teacher effects, are not adequately considered in most evaluation designs. Some studies mention and give a subjective judgment as to the nature of the problem, but this is descriptive at the most. Hardly any of the studies actually do anything analytical, and because these are such important potential confounding variables, this presents a serious challenge to the efficacy of these studies. Figure 5-5 shows how attention to these factors varies

FIGURE 5-5 Treatment of implementation components by program type.

NOTE: PD = professional development.

across program categories among NSF-supported, UCSMP, and studies of commercial materials. In general, evaluations of NSF-supported studies were the most likely to measure these variables; UCSMP had the most standardized use of methods to do so across studies; and commercial material evaluators seldom reported on issues of implementation fidelity.

Identification of a Set of Outcome Measures and Forms of Disaggregation

Using the selected student outcomes identified in the program theory, one must conduct an impact assessment that refers to the design and measurement of student outcomes. In addition to selecting what outcomes should be measured within one’s program theory, one must determine how these outcomes are measured, when those measures are collected, and what

purpose they serve from the perspective of the participants. In the case of curricular evaluation, there are significant issues involved in how these measures are reported. To provide insight into the level of curricular validity, many evaluators prefer to report results by topic, content strand, or item cluster. These reports often present the level of specificity of outcome needed to inform curriculum designers, especially when efforts are made to document patterns of errors, distribution of results across multiple choices, or analyses of student methods. In these cases, whole test scores may mask essential differences in impact among curricula at the level of content topics, reporting only average performance.

On the other hand, many large-scale assessments depend on methods of test equating that rely on whole test scores and make comparative interpretations of different test administrations by content strands of questionable reliability. Furthermore, there are questions such as whether to present only gain scores effect sizes, how to link pretests and posttests, and how to determine the relative curricular sensitivity of various outcome measures.

The findings of comparative studies are reported in terms of the outcome measure(s) collected. To describe the nature of the database with regard to outcome measures and to facilitate our analyses of the studies, we classified each of the included studies on four outcome measure dimensions:

Total score reported;

Disaggregation of content strands, subtest, performance level, SES, or gender;

Outcome measure that was specific to curriculum; and

Use of multiple outcome measures.

Most studies reported a total score, but we did find studies that reported only subtest scores or only scores on an item-by-item basis. For example, in the Ben-Chaim et al. (1998) evaluation study of Connected Math, the authors were interested in students’ proportional reasoning proficiency as a result of use of this curriculum. They asked students from eight seventh-grade classes of CMP and six seventh-grade classes from the control group to solve a variety of tasks categorized as rate and density problems. The authors provide precise descriptions of the cognitive challenges in the items; however, they do not explain if the problems written up were representative of performance on a larger set of items. A special rating form was developed to code responses in three major categories (correct answer, incorrect answer, and no response), with subcategories indicating the quality of the work that accompanied the response. No reports on reliability of coding were given. Performance on standardized tests indicated that control students’ scores were slightly higher than CMP at the beginning of the

year and lower at the end. Twenty-five percent of the experimental group members were interviewed about their approaches to the problems. The CMP students outperformed the control students (53 percent versus 28 percent) overall in providing the correct answers and support work, and 27 percent of the control group gave an incorrect answer or showed incorrect thinking compared to 13 percent of the CMP group. An item-level analysis permitted the researchers to evaluate the actual strategies used by the students. They reported, for example, that 82 percent of CMP students used a “strategy focused on package price, unit price, or a combination of the two; those effective strategies were used by only 56 of 91 control students (62 percent)” (p. 264).

The use of item or content strand-level comparative reports had the advantage that they permitted the evaluators to assess student learning strategies specific to a curriculum’s program theory. For example, at times, evaluators wanted to gauge the effectiveness of using problems different from those on typical standardized tests. In this case, problems were drawn from familiar circumstances but carefully designed to create significant cognitive challenges, and assess how well the informal strategies approach in CMP works in comparison to traditional instruction. The disadvantages of such an approach include the use of only a small number of items and the concerns for reliability in scoring. These studies seem to represent a method of creating hybrid research models that build on the detailed analyses possible using case studies, but still reporting on samples that provide comparative data. It possibly reflects the concerns of some mathematicians and mathematics educators that the effectiveness of materials needs to be evaluated relative to very specific, research-based issues on learning and that these are often inadequately measured by multiple-choice tests. However, a decision not to report total scores led to a trade-off in the reliability and representativeness of the reported data, which must be addressed to increase the objectivity of the reports.

Second, we coded whether outcome data were disaggregated in some way. Disaggregation involved reporting data on dimensions such as content strand, subtest, test item, ethnic group, performance level, SES, and gender. We found disaggregated results particularly helpful in understanding the findings of studies that found main effects, and also in examining patterns across studies. We report the results of the studies’ disaggregation by content strand in our reports of effects. We report the results of the studies’ disaggregation by subgroup in our discussions of generalizability.

Third, we coded whether a study used an outcome measure that the evaluator reported as being sensitive to a particular treatment—this is a subcategory of what was defined in our framework as “curricular validity of measures.” In such studies, the rationale was that readily available measures such as state-mandated tests, norm-referenced standardized tests, and

college entrance examinations do not measure some of the aims of the program under study. A frequently cited instance of this was that “off the shelf” instruments do not measure well students’ ability to apply their mathematical knowledge to problems embedded in complex settings. Thus, some studies constructed a collection of tasks that assessed this ability and collected data on it (Ben-Chaim et al., 1998; Huntley et al., 2000).

Finally, we recorded whether a study used multiple outcome measures. Some studies used a variety of achievement measures and other studies reported on achievement accompanied by measures such as subsequent course taking or various types of affective measures. For example, Carroll (2001, p. 47) reported results on a norm-referenced standardized achievement test as well as a collection of tasks developed in other studies.

A study by Huntley et al. (2000) illustrates how a variety of these techniques were combined in their outcome measures. They developed three assessments. The first emphasized contextualized problem solving based on items from the American Mathematical Association of Two-Year Colleges and others; the second assessment was on context-free symbolic manipulation and a third part requiring collaborative problem solving. To link these measures to the overall evaluation, they articulated an explicit model of cognition based on how one links an applied situation to mathematical activity through processes of formulation and interpretation. Their assessment strategy permitted them to investigate algebraic reasoning as an ability to use algebraic ideas and techniques to (1) mathematize quantitative problem situations, (2) use algebraic principles and procedures to solve equations, and (3) interpret results of reasoning and calculations.

In presenting their data comparing performance on Core-Plus and traditional curriculum, they presented both main effects and comparisons on subscales. Their design of outcome measures permitted them to examine differences in performance with and without context and to conclude with statements such as “This result illustrates that CPMP students perform better than control students when setting up models and solving algebraic problems presented in meaningful contexts while having access to calculators, but CPMP students do not perform as well on formal symbol-manipulation tasks without access to context cues or calculators” (p. 349). The authors go on to present data on the relationship between knowing how to plan or interpret solutions and knowing how to carry them out. The correlations between these variables were weak but significantly different (0.26 for control groups and 0.35 for Core-Plus). The advantage of using multiple measures carefully tied to program theory is that they can permit one to test fine content distinctions that are likely to be the level of adjustments necessary to fine tune and improve curricular programs.

Another interesting approach to the use of outcome measures is found in the UCSMP studies. In many of these studies, evaluators collected infor-

TABLE 5-2 Mean Percentage Correct on the Subject Tests

mation from teachers’ reports and chapter reviews as to whether topics for items on the posttests were taught, calling this an “opportunity to learn” measure. The authors reported results from three types of analyses: (1) total test scores, (2) fair test scores (scores reported by program but only on items on topics taught), and (3) conservative test scores (scores on common items taught in both). Table 5-2 reports on the variations across the multiple- choice test scores for the Geometry study (Thompson et al., 2003) on a standardized test, High School Subject Tests-Geometry Form B , and the UCSMP-constructed Geometry test, and for the Advanced Algebra Study on the UCSMP-constructed Advanced Algebra test (Thompson et al., 2001). The table shows the mean scores for UCSMP classes and comparison classes. In each cell, mean percentage correct is reported first by whole test, then by fair test, and then by conservative test.

The authors explicitly compare the items from the standard Geometry test with the items from the UCSMP test and indicate overlap and difference. They constructed their own test because, in their view, the standard test was not adequately balanced among skills, properties, and real-world uses. The UCSMP test included items on transformations, representations, and applications that were lacking in the national test. Only five items were taught by all teachers; hence in the case of the UCSMP geometry test, there is no report on a conservative test. In the Advanced Algebra evaluation, only a UCSMP-constructed test was viewed as appropriate to cover the treatment of the prior material and alignment to the goals of the new course. These data sets demonstrate the challenge of selecting appropriate outcome measures, the sensitivity of the results to those decisions, and the importance of full disclosure of decision-making processes in order to permit readers to assess the implications of the choices. The methodology utilized sought to ensure that the material in the course was covered adequately by treatment teachers while finding ways to make comparisons that reflected content coverage.

Only one study reported on its outcomes using embedded assessment items employed over the course of the year. In a study of Saxon and UCSMP, Peters (1992) (EX) studied the use of these materials with two classrooms taught by the same teacher. In this small study, he randomly assigned students to treatment groups and then measured their performance on four unit tests composed of items common to both curricula and their progress on the Orleans-Hanna Algebraic Prognosis Test.

Peters’ study showed no significant difference in placement scores between Saxon and UCSMP on the posttest, but did show differences on the embedded assessment. Figure 5-6 (Peters, 1992, p. 75) shows an interesting display of the differences on a “continuum” that shows both the direction and magnitude of the differences and provides a level of concept specificity missing in many reports. This figure and a display ( Figure 5-7 ) in a study by Senk (1991, p. 18) of students’ mean scores on Curriculum A versus Curriculum B with a 10 percent range of differences marked represent two excellent means to communicate the kinds of detailed content outcome information that promises to be informative to curriculum writers, publishers, and school decision makers. In Figure 5-7 , 16 items listed by number were taken from the Second International Mathematics Study. The Functions, Statistics, and Trigonometry sample averaged 41 percent correct on these items whereas the U.S. precalculus sample averaged 38 percent. As shown in the figure, differences of 10 percent or less fall inside the banded area and greater than 10 percent fall outside, producing a display that makes it easy for readers and designers to identify the relative curricular strengths and weaknesses of topics.

While we value detailed outcome measure information, we also recognize the importance of examining curricular impact on students’ standardized test performance. Many developers, but not all, are explicit in rejecting standardized tests as adequate measures of the outcomes of their programs, claiming that these tests focus on skills and manipulations, that they are overly reliant on multiple-choice questions, and that they are often poorly aligned to new content emphases such as probability and statistics, transformations, use of contextual problems and functions, and process skills, such as problem solving, representation, or use of calculators. However, national and state tests are being revised to include more content on these topics and to draw on more advanced reasoning. Furthermore, these high-stakes tests are of major importance in school systems, determining graduation, passing standards, school ratings, and so forth. For this reason, if a curricular program demonstrated positive impact on such measures, we referred to that in Chapter 3 as establishing “curricular alignment with systemic factors.” Adequate performance on these measures is of paramount importance to the survival of reform (to large groups of parents and

FIGURE 5-6 Continuum of criterion score averages for studied programs.

SOURCE: Peters (1992, p. 75).

school administrators). These examples demonstrate how careful attention to outcomes measures is an essential element of valid evaluation.

In Table 5-3 , we document the number of studies using a variety of types of outcome measures that we used to code the data, and also report on the types of tests used across the studies.

FIGURE 5-7 Achievement (percentage correct) on Second International Mathematics Study (SIMS) items by U.S. precalculus students and functions, statistics, and trigonometry (FST) students.

SOURCE: Re-created from Senk (1991, p. 18).

TABLE 5-3 Number of Studies Using a Variety of Outcome Measures by Program Type

A Choice of Statistical Tests, Including Statistical Significance and Effect Size

In our first review of the studies, we coded what methods of statistical evaluation were used by different evaluators. Most common were t-tests; less frequently one found Analysis of Variance (ANOVA), Analysis of Co-

FIGURE 5-8 Statistical tests most frequently used.

variance (ANCOVA), and chi-square tests. In a few cases, results were reported using multiple regression or hierarchical linear modeling. Some used multiple tests; hence the total exceeds 63 ( Figure 5-8 ).

One of the difficult aspects of doing curriculum evaluations concerns using the appropriate unit both in terms of the unit to be randomly assigned in an experimental study and the unit to be used in statistical analysis in either an experimental or quasi-experimental study.

For our purposes, we made the decision that unless the study concerned an intact student population such as the freshman at a single university, where a student comparison was the correct unit, we believed that for statistical tests, the unit should be at least at the classroom level. Judgments were made for each study as to whether the appropriate unit was utilized. This question is an important one because statistical significance is related to sample size, and as a result, studies that inappropriately use the student as the unit of analysis could be concluding significant differences where they are not present. For example, if achievement differences between two curricula are tested in 16 classrooms with 400 students, it will always be easier to show significant differences using scores from those 400 students than using 16 classroom means.

Fifty-seven studies used students as the unit of analysis in at least one test of significance. Three of these were coded as correct because they involved whole populations. In all, 10 studies were coded as using the

TABLE 5-4 Performance on Applied Algebra Problems with Use of Calculators, Part 1

TABLE 5-5 Reanalysis of Algebra Performance Data

correct unit of analysis; hence, 7 studies used teachers or classes, or schools. For some studies where multiple tests were conducted, a judgment was made as to whether the primary conclusions drawn treated the unit of analysis adequately. For example, Huntley et al. (2000) compared the performance of CPMP students with students in a traditional course on a measure of ability to formulate and use algebraic models to answer various questions about relationships among variables. The analysis used students as the unit of analysis and showed a significant difference, as shown in Table 5-4 .

To examine the robustness of this result, we reanalyzed the data using an independent sample t-test and a matched pairs t-test with class means as the unit of analysis in both tests ( Table 5-5 ). As can be seen from the analyses, in neither statistical test was the difference between groups found to be significantly different (p < .05), thus emphasizing the importance of using the correct unit in analyzing the data.

Reanalysis of student-level data using class means will not always result

TABLE 5-6 Mean Percentage Correct on Entire Multiple-Choice Posttest: Second Edition and Non-UCSMP

in a change in finding. Furthermore, using class means as the unit of analysis does not suggest that significant differences will not be found. For example, a study by Thompson et al. (2001) compared the performance of UCSMP students with the performance of students in a more traditional program across several measures of achievement. They found significant differences between UCSMP students and the non-UCSMP students on several measures. Table 5-6 shows results of an analysis of a multiple-choice algebraic posttest using class means as the unit of analysis. Significant differences were found in five of eight separate classroom comparisons, as shown in the table. They also found a significant difference using a matched-pairs t-test on class means.

The lesson to be learned from these reanalyses is that the choice of unit of analysis and the way the data are aggregated can impact study findings in important ways including the extent to which these findings can be generalized. Thus it is imperative that evaluators pay close attention to such considerations as the unit of analysis and the way data are aggregated in the design, implementation, and analysis of their studies.

Second, effect size has become a relatively common and standard way of gauging the practical significance of the findings. Statistical significance only indicates whether the main-level differences between two curricula are large enough to not be due to chance, assuming they come from the same population. When statistical differences are found, the question remains as to whether such differences are large enough to consider. Because any innovation has its costs, the question becomes one of cost-effectiveness: Are the differences in student achievement large enough to warrant the costs of change? Quantifying the practical effect once statistical significance is established is one way to address this issue. There is a statistical literature for doing this, and for the purposes of this review, the committee simply noted whether these studies have estimated such an effect. However, the committee further noted that in conducting meta-analyses across these studies, effect size was likely to be of little value. These studies used an enormous variety of outcome measures, and even using effect size as a means to standardize units across studies is not sensible when the measures in each

study address such a variety of topics, forms of reasoning, content levels, and assessment strategies.

We note very few studies drew upon the advances in methodologies employed in modeling, which include causal modeling, hierarchical linear modeling (Bryk and Raudenbush, 1992; Bryk et al., 1993), and selection bias modeling (Heckman and Hotz, 1989). Although developing detailed specifications for these approaches is beyond the scope of this review, we wish to emphasize that these methodological advances should be considered within future evaluation designs.

Results and Limitations to Generalizability Resulting from Design Constraints

One also must consider what generalizations can be drawn from the results (Campbell and Stanley, 1966; Caporaso and Roos, 1973; and Boruch, 1997). Generalization is a matter of external validity in that it determines to what populations the study results are likely to apply. In designing an evaluation study, one must carefully consider, in the selection of units of analysis, how various characteristics of those units will affect the generalizability of the study. It is common for evaluators to conflate issues of representativeness for the purpose of generalizability (external validity) and comparativeness (the selection of or adjustment for comparative groups [internal validity]). Not all studies must be representative of the population served by mathematics curricula to be internally valid. But, to be generalizable beyond restricted communities, representativeness must be obtained by the random selection of the basic units. Clearly specifying such limitations to generalizability is critical. Furthermore, on the basis of equity considerations, one must be sure that if overall effectiveness is claimed, that the studies have been conducted and analyzed with reference of all relevant subgroups.

Thus, depending on the design of a study, its results may be limited in generalizability to other populations and circumstances. We identified four typical kinds of limitations on the generalizability of studies and coded them to determine, on the whole, how generalizable the results across studies might be.

First, there were studies whose designs were limited by the ability or performance level of the students in the samples. It was not unusual to find that when new curricula were implemented at the secondary level, schools kept in place systems of tracking that assigned the top students to traditional college-bound curriculum sequences. As a result, studies either used comparative groups who were matched demographically but less skilled than the population as a whole, in relation to prior learning, or their results compared samples of less well-prepared students to samples of students

with stronger preparations. Alternatively, some studies reported on the effects of curricula reform on gifted and talented students or on college-attending students. In these cases, the study results would also limit the generalizability of the results to similar populations. Reports using limited samples of students’ ability and prior performance levels were coded as a limitation to the generalizability of the study.

For example, Wasman (2000) conducted a study of one school (six teachers) and examined the students’ development of algebraic reasoning after one (n=100) and two years (n=73) in CMP. In this school, the top 25 percent of the students are counseled to take a more traditional algebra course, so her experimental sample, which was 61 percent white, 35 percent African American, 3 percent Asian, and 1 percent Hispanic, consisted of the lower 75 percent of the students. She reported on the student performance on the Iowa Algebraic Aptitude Test (IAAT) (1992), in the subcategories of interpreting information, translating symbols, finding relationships, and using symbols. Results for Forms 1 and 2 of the test, for the experimental and norm group, are shown in Table 5-7 for 8th graders.

In our coding of outcomes, this study was coded as showing no significant differences, although arguably its results demonstrate a positive set of

TABLE 5-7 Comparing Iowa Algebraic Aptitude Test (IAAT) Mean Scores of the Connected Mathematics Project Forms 1 and 2 to the Normative Group (8th Graders)

outcomes as the treatment group was weaker than the control group. Had the researcher used a prior achievement measure and a different statistical technique, significance might have been demonstrated, although potential teacher effects confound interpretations of results.

A second limitation to generalizability was when comparative studies resided entirely at curriculum pilot site locations, where such sites were developed as a means to conduct formative evaluations of the materials with close contact and advice from teachers. Typically, pilot sites have unusual levels of teacher support, whether it is in the form of daily technical support in the use of materials or technology or increased quantities of professional development. These sites are often selected for study because they have established cooperative agreements with the program developers and other sources of data, such as classroom observations, are already available. We coded whether the study was conducted at a pilot site to signal potential limitations in generalizability of the findings.

Third, studies were also coded as being of limited generalizability if they failed to disaggregate their data by socioeconomic class, race, gender, or some other potentially significant sources of restriction on the claims. We recorded the categories in which disaggregation occurred and compiled their frequency across the studies. Because of the need to open the pipeline to advanced study in mathematics by members of underrepresented groups, we were particularly concerned about gauging the extent to which evaluators factored such variables into their analysis of results and not just in terms of the selection of the sample.

Of the 46 included studies of NSF-supported curricula, 19 disaggregated their data by student subgroup. Nine of 17 studies of commercial materials disaggregated their data. Figure 5-9 shows the number of studies that disaggregated outcomes by race or ethnicity, SES, gender, LEP, special education status, or prior achievement. Studies using multiple categories of disaggregation were counted multiple times by program category.

The last category of restricted generalization occurred in studies of limited sample size. Although such studies may have provided more indepth observations of implementation and reports on professional development factors, the smaller numbers of classrooms and students in the study would limit the extent of generalization that could be drawn from it. Figure 5-10 shows the distribution of sizes of the samples in terms of numbers of students by study type.

Summary of Results by Student Achievement Among Program Types

We present the results of the studies as a means to further investigate their methodological implications. To this end, for each study, we counted across outcome measures the number of findings that were positive, nega-

FIGURE 5-9 Disaggregation of subpopulations.

FIGURE 5-10 Proportion of studies by sample size and program.

tive, or indeterminate (no significant difference) and then calculated the proportion of each. We represented the calculation of each study as a triplet (a, b, c) where a indicates the proportion of the results that were positive and statistically significantly stronger than the comparison program, b indicates the proportion that were negative and statistically significantly weaker than the comparison program, and c indicates the proportion that showed no significant difference between the treatment and the comparative group. For studies with a single outcome measure, without disaggregation by content strand, the triplet is always composed of two zeros and a single one. For studies with multiple measures or disaggregation by content strand, the triplet is typically a set of three decimal values that sum to one. For example, a study with one outcome measure in favor of the experimental treatment would be coded (1, 0, 0), while one with multiple measures and mixed results more strongly in favor of the comparative curriculum might be listed as (.20, .50, .30). This triplet would mean that for 20 percent of the comparisons examined, the evaluators reported statistically significant positive results, for 50 percent of the comparisons the results were statistically significant in favor of the comparison group, and for 30 percent of the comparisons no significant difference were found. Overall, the mean score on these distributions was (.54, .07, .40), indicating that across all the studies, 54 percent of the comparisons favored the treatment, 7 percent favored the comparison group, and 40 percent showed no significant difference. Table 5-8 shows the comparison by curricular program types. We present the results by individual program types, because each program type relies on a similar program theory and hence could lead to patterns of results that would be lost in combining the data. If the studies of commercial materials are all grouped together to include UCSMP, their pattern of results is (.38, .11, .51). Again we emphasize that due to our call for increased methodological rigor and the use of multiple methods, this result is not sufficient to establish the curricular effectiveness of these programs as a whole with adequate certainty.

We caution readers that these results are summaries of the results presented across a set of evaluations that meet only the standard of at least

TABLE 5-8 Comparison by Curricular Program Types

minimally methodologically adequate . Calculations of statistical significance of each program’s results were reported by the evaluators; we have made no adjustments for weaknesses in the evaluations such as inappropriate use of units of analysis in calculating statistical significance. Evaluations that consistently used the correct unit of analysis, such as UCSMP, could have fewer reports of significant results as a consequence. Furthermore, these results are not weighted by study size. Within any study, the results pay no attention to comparative effect size or to the established credibility of an outcome measure. Similarly, these results do not take into account differences in the populations sampled, an important consideration in generalizing the results. For example, using the same set of studies as an example, UCSMP studies used volunteer samples who responded to advertisements in their newsletters, resulting in samples with disproportionately Caucasian subjects from wealthier schools compared to national samples. As a result, we would suggest that these results are useful only as baseline data for future evaluation efforts. Our purpose in calculating these results is to permit us to create filters from the critical decision points and test how the results change as one applies more rigorous standards.

Given that none of the studies adequately addressed all of the critical criteria, we do not offer these results as definitive, only suggestive—a hypothesis for further study. In effect, given the limitations of time and support, and the urgency of providing advice related to policy, we offer this filtering approach as an informal meta-analytic technique sufficient to permit us to address our primary task, namely, evaluating the quality of the evaluation studies.

This approach reflects the committee’s view that to deeply understand and improve methodology, it is necessary to scrutinize the results and to determine what inferences they provide about the conduct of future evaluations. Analogous to debates on consequential validity in testing, we argue that to strengthen methodology, one must consider what current methodologies are able (or not able) to produce across an entire series of studies. The remainder of the chapter is focused on considering in detail what claims are made by these studies, and how robust those claims are when subjected to challenge by alternative hypothesis, filtering by tests of increasing rigor, and examining results and patterns across the studies.

Alternative Hypotheses on Effectiveness

In the spirit of scientific rigor, the committee sought to consider rival hypotheses that could explain the data. Given the weaknesses in the designs generally, often these alternative hypotheses cannot be dismissed. However, we believed that only after examining the configuration of results and

alternative hypotheses can the next generation of evaluations be better informed and better designed. We began by generating alternative hypotheses to explain the positive directionality of the results in favor of experimental groups. Alternative hypotheses included the following:

The teachers in the experimental groups tended to be self-selecting early adopters, and thus able to achieve effects not likely in regular populations.

Changes in student outcomes reflect the effects of professional development instruction, or level of classroom support (in pilot sites), and thus inflate the predictions of effectiveness of curricular programs.

Hawthorne effect (Franke and Kaul, 1978) occurs when treatments are compared to everyday practices, due to motivational factors that influence experimental participants.

The consistent difference is due to the coherence and consistency of a single curricular program when compared to multiple programs.

The significance level is only achieved by the use of the wrong unit of analysis to test for significance.

Supplemental materials or new teaching techniques produce the results and not the experimental curricula.

Significant results reflect inadequate outcome measures that focus on a restricted set of activities.

The results are due to evaluator bias because too few evaluators are independent of the program developers.

At the same time, one could argue that the results actually underestimate the performance of these materials and are conservative measures, and their alternative hypotheses also deserve consideration:

Many standardized tests are not sensitive to these curricular approaches, and by eliminating studies focusing on affect, we eliminated a key indicator of the appeal of these curricula to students.

Poor implementation or increased demands on teachers’ knowledge dampens the effects.

Often in the experimental treatment, top-performing students are missing as they are advised to take traditional sequences, rendering the samples unequal.

Materials are not well aligned with universities and colleges because tests for placement and success in early courses focus extensively on algebraic manipulation.

Program implementation has been undercut by negative publicity and the fears of parents concerning change.

There are also a number of possible hypotheses that may be affecting the results in either direction, and we list a few of these:

Examining the role of the teacher in curricular decision making is an important element in effective implementation, and design mandates of evaluation design make this impossible (and the positives and negatives or single- versus dual-track curriculum as in Lundin, 2001).

Local tests that are sensitive to the curricular effects typically are not mandatory and hence may lead to unpredictable performance by students.

Different types and extent of professional development may affect outcomes differentially.

Persistence or attrition may affect the mean scores and are often not considered in the comparative analyses.

One could also generate reasons why the curricular programs produced results showing no significance when one program or the other is actually more effective. This could include high degrees of variability in the results, samples that used the correct unit of analysis but did not obtain consistent participation across enough cases, implementation that did not show enough fidelity to the measures, or outcome measures insensitive to the results. Again, subsequent designs should be better informed by these findings to improve the likelihood that they will produce less ambiguous results and replication of studies could also give more confidence in the findings.

It is beyond the scope of this report to consider each of these alternative hypotheses separately and to seek confirmation or refutation of them. However, in the next section, we describe a set of analyses carried out by the committee that permits us to examine and consider the impact of various critical evaluation design decisions on the patterns of outcomes across sets of studies. A number of analyses shed some light on various alternative hypotheses and may inform the conduct of future evaluations.

Filtering Studies by Critical Decision Points to Increase Rigor

In examining the comparative studies, we identified seven critical decision points that we believed would directly affect the rigor and efficacy of the study design. These decision points were used to create a set of 16 filters. These are listed as the following questions:

Was there a report on comparability relative to SES?

Was there a report on comparability of samples relative to prior knowledge?

Was there a report on treatment fidelity?

Was professional development reported on?

Was the comparative curriculum specified?

Was there any attempt to report on teacher effects?

Was a total test score reported?

Was total test score(s) disaggregated by content strand?

Did the outcome measures match the curriculum?

Were multiple tests used?

Was the appropriate unit of analysis used in their statistical tests?

Did they estimate effect size for the study?

Was the generalizability of their findings limited by use of a restricted range of ability levels?

Was the generalizability of their findings limited by use of pilot sites for their study?

Was the generalizability of their findings limited by not disaggregating their results by subgroup?

Was the generalizability of their findings limited by use of small sample size?

The studies were coded to indicate if they reported having addressed these considerations. In some cases, the decision points were coded dichotomously as present or absent in the studies, and in other cases, the decision points were coded trichotomously, as description presented, absent, or statistically adjusted for in the results. For example, a study may or may not report on the comparability of the samples in terms of race, ethnicity, or socioeconomic status. If a report on SES was given, the study was coded as “present” on this decision; if a report was missing, it was coded as “absent”; and if SES status or ethnicity was used in the analysis to actually adjust outcomes, it was coded as “adjusted for.” For each coding, the table that follows reports the number of studies that met that condition, and then reports on the mean percentage of statistically significant results, and results showing no significant difference for that set of studies. A significance test is run to see if the application of the filter produces changes in the probability that are significantly different. 5

In the cases in which studies are coded into three distinct categories—present, absent, and adjusted for—a second set of filters is applied. First, the studies coded as present or adjusted for are combined and compared to those coded as absent; this is what we refer to as a weak test of the rigor of the study. Second, the studies coded as present or absent are combined and compared to those coded as adjusted for. This is what we refer to as a strong test. For dichotomous codings, there can be as few as three compari-

sons, and for trichotomous codings, there can be nine comparisons with accompanying tests of significance. Trichotomous codes were used for adjustments for SES and prior knowledge, examining treatment fidelity, professional development, teacher effects, and reports on effect sizes. All others were dichotomous.

NSF Studies and the Filters

For example, there were 11 studies of NSF-supported curricula that simply reported on the issues of SES in creating equivalent samples for comparison, and for this subset the mean probabilities of getting positive, negative, or results showing no significant difference were (.47, .10, .43). If no report of SES was supplied (n= 21), those probabilities become (.57, .07, .37), indicating an increase in positive results and a decrease in results showing no significant difference. When an adjustment is made in outcomes based on differences in SES (n=14), the probabilities change to (.72, .00, .28), showing a higher likelihood of positive outcomes. The probabilities that result from filtering should always be compared back to the overall results of (.59, .06, .35) (see Table 5-8 ) so as to permit one to judge the effects of more rigorous methodological constraints. This suggests that a simple report on SES without adjustment is least likely to produce positive outcomes; that is, no report produces the outcomes next most likely to be positive and studies that adjusted for SES tend to have a higher proportion of their comparisons producing positive results.

The second method of applying the filter (the weak test for rigor) for the treatment of the adjustment of SES groups compares the probabilities when a report is either given or adjusted for compared to when no report is offered. The combined percentage of a positive outcome of a study in which SES is reported or adjusted for is (.61, .05, .34), while the percentage for no report remains as reported previously at (.57, .07, .37). A final filter compares the probabilities of the studies in which SES is adjusted for with those that either report it only or do not report it at all. Here we compare the percentage of (.72, .00, .28) to (.53, .08, .37) in what we call a strong test. In each case we compared the probability produced by the whole group to those of the filtered studies and conducted a test of the differences to determine if they were significant. These differences were not significant. These findings indicate that to date, with this set of studies, there is no statistically significant difference in results when one reports or adjusts for changes in SES. It appears that by adjusting for SES, one sees increases in the positive results, and this result deserves a closer examination for its implications should it prove to hold up over larger sets of studies.

We ran tests that report the impact of the filters on the number of studies, the percentage of studies, and the effects described as probabilities

for each of the three study categories, NSF-supported and commercially generated with UCSMP included. We claim that when a pattern of probabilities of results does not change after filtering, one can have more confidence in that pattern. When the pattern of results changes, there is a need for an explanatory hypothesis, and that hypothesis can shed light on experimental design. We propose that this “filtering process” constitutes a test of the robustness of the outcome measures subjected to increasing degrees of rigor by using filtering.

Results of Filtering on Evaluations of NSF-Supported Curricula

For the NSF-supported curricular programs, out of 15 filters, 5 produced a probability that differed significantly at the p<.1 level. The five filters were for treatment fidelity, specification of control group, choosing the appropriate statistical unit, generalizability for ability, and generalizability based on disaggregation by subgroup. For each filter, there were from three to nine comparisons, as we examined how the probabilities of outcomes change as tests were more stringent and across the categories of positive results, negative results, and results with no significant differences. Out of a total of 72 possible tests, only 11 produced a probability that differed significantly at the p < .1 level. With 85 percent of the comparisons showing no significant difference after filtering, we suggest the results of the studies were relatively robust in relation to these tests. At the same time, when rigor is increased for the five filters just listed, the results become generally more ambiguous and signal the need for further research with more careful designs.

Studies of Commercial Materials and the Filters

To ensure enough studies to conduct the analysis (n=17), our filtering analysis of the commercially generated studies included UCSMP (n=8). In this case, there were six filters that produced a probability that differed significantly at the p < .1 level. These were treatment fidelity, disaggregation by content, use of multiple tests, use of effect size, generalizability by ability, and generalizability by sample size. In this case, because there were no studies in some possible categories, there were a total of 57 comparisons, and 9 displayed significant differences in the probabilities after filtering at the p < .1 level. With 84 percent of the comparisons showing no significant difference after filtering, we suggest the results of the studies were relatively robust in relation to these tests. Table 5-9 shows the cases in which significant differences were recorded.

Impact of Treatment Fidelity on Probabilities

A few of these differences are worthy of comment. In the cases of both the NSF-supported and commercially generated curricula evaluation studies, studies that reported treatment fidelity differed significantly from those that did not. In the case of the studies of NSF-supported curricula, it appeared that a report or adjustment on treatment fidelity led to proportions with less positive effects and more results showing no significant differences. We hypothesize that this is partly because larger studies often do not examine actual classroom practices, but can obtain significance more easily due to large sample sizes.

In the studies of commercial materials, the presence or absence of measures of treatment fidelity worked differently. Studies reporting on or adjusting for treatment fidelity tended to have significantly higher probabilities in favor of experimental treatment, less positive effects in fewer of the comparative treatments, and more likelihood of results with no significant differences. We hypothesize, and confirm with a separate analysis, that this is because UCSMP frequently reported on treatment fidelity in their designs while study of Saxon typically did not, and the change represents the preponderance of these different curricular treatments in the studies of commercially generated materials.

Impact of Identification of Curricular Program on Probabilities

The significant differences reported under specificity of curricular comparison also merit discussion for studies of NSF-supported curricula. When the comparison group is not specified, a higher percentage of mean scores in favor of the experimental curricula is reported. In the studies of commercial materials, a failure to name specific curricular comparisons also produced a higher percentage of positive outcomes for the treatment, but the difference was not statistically significant. This suggests the possibility that when a specified curriculum is compared to an unspecified curriculum, reports of impact may be inflated. This finding may suggest that in studies of effectiveness, specifying comparative treatments would provide more rigorous tests of experimental approaches.

When studies of commercial materials disaggregate their results of content strands or use multiple measures, their reports of positive outcomes increase, the negative outcomes decrease, and in one case, the results show no significant differences. Percentage of significant difference was only recorded in one comparison within each one of these filters.

TABLE 5-9 Cases of Significant Differences

Impact of Units of Analysis on Probabilities 6

For the evaluations of the NSF-supported materials, a significant difference was reported on the outcomes for the studies that used the correct unit of analysis compared to those that did not. The percentage for those with the correct unit were (.30, .40, .30) compared to (.63, .01, .36) for those that used the incorrect result. These results suggest that our prediction that using the correct unit of analysis would decrease the percentage of positive outcomes is likely to be correct. It also suggests that the most serious threat to the apparent conclusions of these studies comes from selecting an incorrect unit of analysis. It causes a decrease in favorable results, making the results more ambiguous, but never reverses the direction of the effect. This is a concern that merits major attention in the conduct of further studies.

For the commercially generated studies, most of the ones coded with the correct unit of analysis were UCSMP studies. Because of the small number of studies involved, we could not break out from the overall filtering of studies of commercial materials, but report this issue to assist readers in interpreting the relative patterns of results.

Impact of Generalizability on Probabilities

Both types of studies yielded significant differences for some of the comparisons coded as restrictions to generalizability. Investigating these is important in order to understand the effects of these curricular programs on different subpopulations of students. In the case of the studies of commercially generated materials, significantly different results occurred in the categories of ability and sample size. In the studies of NSF-supported materials, the significant differences occurred in ability and disaggregation by subgroups.

In relation to generalizability, the studies of NSF-supported curricula reported significantly more positive results in favor of the treatment when they included all students. Because studies coded as “limited by ability” were restricted either by focusing only on higher achieving students or on lower achieving students, we sorted these two groups. For higher performing students (n=3), the probabilities of effects were (.11, .67, .22). For lower

performing students (n=2), the probabilities were (.39, .025, .59). The first two comparisons are significantly different at p < .05. These findings are based on only a total of five studies, but they suggest that these programs may be serving the weaker ability students more effectively than the stronger ability students, serving both less well than they serve whole heterogeneous groups. For the studies of commercial materials, there were only three studies that were restricted to limited populations. The results for those three studies were (.23, .41, .32) and for all students (n=14) were (.42, .53, .09). These studies were significantly different at p = .004. All three studies included UCSMP and one also included Saxon and was limited by serving primarily high-performing students. This means both categories of programs are showing weaker results when used with high-ability students.

Finally, the studies on NSF-supported materials were disaggregated by subgroups for 28 studies. A complete analysis of this set follows, but the studies that did not report results disaggregated by subgroup generated probabilities of results of (.48, .09, .43) whereas those that did disaggregate their results reported (.76, 0, .24). These gains in positive effects came from significant losses in reporting no significant differences. Studies of commercial materials also reported a small decrease in likelihood of negative effects for the comparison program when disaggregation by subgroup is reported offset by increases in positive results and results with no significant differences, although these comparisons were not significantly different. A further analysis of this topic follows.

Overall, these results suggest that increased rigor seems to lead in general to less strong outcomes, but never reports of completely contrary results. These results also suggest that in recommending design considerations to evaluators, there should be careful attention to having evaluators include measures of treatment fidelity, considering the impact on all students as well as one particular subgroup; using the correct unit of analysis; and using multiple tests that are also disaggregated by content strand.

Further Analyses

We conducted four further analyses: (1) an analysis of the outcome probabilities by test type; (2) content strands analysis; (3) equity analysis; and (4) an analysis of the interactions of content and equity by grade band. Careful attention to the issues of content strand, equity, and interaction is essential for the advancement of curricular evaluation. Content strand analysis provides the detail that is often lost by reporting overall scores; equity analysis can provide essential information on what subgroups are adequately served by the innovations, and analysis by content and grade level can shed light on the controversies that evolve over time.

Analysis by Test Type

Different studies used varied combinations of outcome measures. Because of the importance of outcome measures on test results, we chose to examine whether the probabilities for the studies changed significantly across different types of outcome measures (national test, local test). The most frequent use of tests across all studies was a combination of national and local tests (n=18 studies), a local test (n=16), and national tests (n=17). Other uses of test combinations were used by three studies or less. The percentages of various outcomes by test type in comparison to all studies are described in Table 5-10 .

These data ( Table 5-11 ) suggest that national tests tend to produce less positive results, and with the resulting gains falling into results showing no significant differences, suggesting that national tests demonstrate less curricular sensitivity and specificity.

TABLE 5-10 Percentage of Outcomes by Test Type

TABLE 5-11 Percentage of Outcomes by Test Type and Program Type

TABLE 5-12 Number of Studies That Disaggregated by Content Strand

Content Strand

Curricular effectiveness is not an all-or-nothing proposition. A curriculum may be effective in some topics and less effective in others. For this reason, it is useful for evaluators to include an analysis of curricular strands and to report on the performance of students on those strands. To examine this issue, we conducted an analysis of the studies that reported their results by content strand. Thirty-eight studies did this; the breakdown is shown in Table 5-12 by type of curricular program and grade band.

To examine the evaluations of these content strands, we began by listing all of the content strands reported across studies as well as the frequency of report by the number of studies at each grade band. These results are shown in Figure 5-11 , which is broken down by content strand, grade level, and program type.

Although there are numerous content strands, some of them were reported on infrequently. To allow the analysis to focus on the key results from these studies, we separated out the most frequently reported on strands, which we call the “major content strands.” We defined these as strands that were examined in at least 10 percent of the studies. The major content strands are marked with an asterisk in the Figure 5-11 . When we conduct analyses across curricular program types or grade levels, we use these to facilitate comparisons.

A second phase of our analysis was to examine the performance of students by content strand in the treatment group in comparison to the control groups. Our analysis was conducted across the major content strands at the level of NSF-supported versus commercially generated, initially by all studies and then by grade band. It appeared that such analysis permitted some patterns to emerge that might prove helpful to future evaluators in considering the overall effectiveness of each approach. To do this, we then coded the number of times any particular strand was measured across all studies that disaggregated by content strand. Then, we coded the proportion of times that this strand was reported as favoring the experimental treatment, favoring the comparative curricula, or showing no significant difference. These data are presented across the major content strands for the NSF-supported curricula ( Figure 5-12 ) and the commercially generated curricula, ( Figure 5-13 ) (except in the case of the elemen-

FIGURE 5-11 Study counts for all content strands.

tary curricula where no data were available) in the forms of percentages, with the frequencies listed in the bars.

The presentation of results by strands must be accompanied by the same restrictions as stated previously. These results are based on studies identified as at least minimally methodologically adequate. The quality of the outcome measures in measuring the content strands has not been examined. Their results are coded in relation to the comparison group in the study and are indicated as statistically in favor of the program, as in favor of the comparative program, or as showing no significant differences. The results are combined across studies with no weighting by study size. Their results should be viewed as a means for the identification of topics for potential future study. It is completely possible that a refinement of methodologies may affect the future patterns of results, so the results are to be viewed as tentative and suggestive.

FIGURE 5-12 Major content strand result: All NSF (n=27).

According to these tentative results, future evaluations should examine whether the NSF-supported programs produce sufficient competency among students in the areas of algebraic manipulation and computation. In computation, approximately 40 percent of the results were in favor of the treatment group, no significant differences were reported in approximately 50 percent of the results, and results in favor of the comparison were revealed 10 percent of the time. Interpreting that final proportion of no significant difference is essential. Some would argue that because computation has not been emphasized, findings of no significant differences are acceptable. Others would suggest that such findings indicate weakness, because the development of the materials and accompanying professional development yielded no significant difference in key areas.

FIGURE 5-13 Major content strand result: All commercial (n=8).

From Figure 5-13 of findings from studies of commercially generated curricula, it appears that mixed results are commonly reported. Thus, in evaluations of commercial materials, lack of significant differences in computations/operations, word problems, and probability and statistics suggest that careful attention should be given to measuring these outcomes in future evaluations.

Overall, the grade band results for the NSF-supported programs—while consistent with the aggregated results—provide more detail. At the elementary level, evaluations of NSF-supported curricula (n=12) report better performance in mathematics concepts, geometry, and reasoning and problem solving, and some weaknesses in computation. No content strand analysis for commercially generated materials was possible. Evaluations

(n=6) at middle grades of NSF-supported curricula showed strength in measurement, geometry, and probability and statistics and some weaknesses in computation. In the studies of commercial materials, evaluations (n=4) reported favorable results in reasoning and problem solving and some unfavorable results in algebraic procedures, contextual problems, and mathematics concepts. Finally, at the high school level, the evaluations (n=9) by content strand for the NSF-supported curricula showed strong favorable results in algebra concepts, reasoning/problem solving, word problems, probability and statistics, and measurement. Results in favor of the control were reported in 25 percent of the algebra procedures and 33 percent of computation measures.

For the studies of commercial materials (n=4), only the geometry results favor the control group 25 percent of the time, with 50 percent having favorable results. Algebra concepts, reasoning, and probability and statistics also produced favorable results.

Equity Analysis of Comparative Studies

When the goal of providing a standards-based curriculum to all students was proposed, most people could recognize its merits: the replacement of dull, repetitive, largely dead-end courses with courses that would lead all students to be able, if desired and earned, to pursue careers in mathematics-reliant fields. It was clear that the NSF-supported projects, a stated goal of which was to provide standards-based courses to all students, called for curricula that would address the problem of too few students persisting in the study of mathematics. For example, as stated in the NSF Request for Proposals (RFP):

Rather than prematurely tracking students by curricular objectives, secondary school mathematics should provide for all students a common core of mainstream mathematics differentiated instructionally by level of abstraction and formalism, depth of treatment and pace (National Science Foundation, 1991, p. 1). In the elementary level solicitation, a similar statement on causes for all students was made (National Science Foundation, 1988, pp. 4-5).

Some, but not enough attention has been paid to the education of students who fall below the average of the class. On the other hand, because the above average students sometimes do not receive a demanding education, it may be incorrectly assumed they are easy to teach (National Science Foundation, 1989, p. 2).

Likewise, with increasing numbers of students in urban schools, and increased demographic diversity, the challenges of equity are equally significant for commercial publishers, who feel increasing pressures to demonstrate the effectiveness of their products in various contexts.

The problem was clearly identified: poorer performance by certain subgroups of students (minorities—non-Asian, LEP students, sometimes females) and a resulting lack of representation of such groups in mathematics-reliant fields. In addition, a secondary problem was acknowledged: Highly talented American students were not being provided adequate challenge and stimulation in comparison with their international counterparts. We relied on the concept of equity in examining the evaluation. Equity was contrasted to equality, where one assumed all students should be treated exactly the same (Secada et al., 1995). Equity was defined as providing opportunities and eliminating barriers so that the membership in a subgroup does not subject one to undue and systematically diminished possibility of success in pursuing mathematical study. Appropriate treatment therefore varies according to the needs of and obstacles facing any subgroup.

Applying the principles of equity to evaluate the progress of curricular programs is a conceptually thorny challenge. What is challenging is how to evaluate curricular programs on their progress toward equity in meeting the needs of a diverse student body. Consider how the following questions provide one with a variety of perspectives on the effectiveness of curricular reform regarding equity:

Does one expect all students to improve performance, thus raising the bar, but possibly not to decrease the gap between traditionally well-served and under-served students?

Does one focus on reducing the gap and devote less attention to overall gains, thus closing the gap but possibly not raising the bar?

Or, does one seek evidence that progress is made on both challenges—seeking progress for all students and arguably faster progress for those most at risk?

Evaluating each of the first two questions independently seems relatively straightforward. When one opts for a combination of these two, the potential for tensions between the two becomes more evident. For example, how can one differentiate between the case in which the gap is closed because talented students are being underchallenged from the case in which the gap is closed because the low-performing students improved their progress at an increased rate? Many believe that nearly all mathematics curricula in this country are insufficiently challenging and rigorous. Therefore achieving modest gains across all ability levels with evidence of accelerated progress by at-risk students may still be criticized for failure to stimulate the top performing student group adequately. Evaluating curricula with regard to this aspect therefore requires judgment and careful methodological attention.

Depending on one’s view of equity, different implications for the collection of data follow. These considerations made examination of the quality of the evaluations as they treated questions of equity challenging for the committee members. Hence we spell out our assumptions as precisely as possible:

Evaluation studies should include representative samples of student demographics, which may require particular attention to the inclusion of underrepresented minority students from lower socioeconomic groups, females, and special needs populations (LEP, learning disabled, gifted and talented students) in the samples. This may require one to solicit participation by particular schools or districts, rather than to follow the patterns of commercial implementation, which may lead to an unrepresentative sample in aggregate.

Analysis of results should always consider the impact of the program on the entire spectrum of the sample to determine whether the overall gains are distributed fairly among differing student groups, and not achieved as improvements in the mean(s) of an identifiable subpopulation(s) alone.

Analysis should examine whether any group of students is systematically less well served by curricular implementation, causing losses or weakening the rate of gains. For example, this could occur if one neglected the continued development of programs for gifted and talented students in mathematics in order to implement programs focused on improving access for underserved youth, or if one improved programs solely for one group of language learners, ignoring the needs of others, or if one’s study systematically failed to report high attrition affecting rates of participation of success or failure.

Analyses should examine whether gaps in scores between significantly disadvantaged or underperforming subgroups and advantaged subgroups are decreasing both in relation to eliminating the development of gaps in the first place and in relation to accelerating improvement for underserved youth relative to their advantaged peers at the upper grades.

In reviewing the outcomes of the studies, the committee reports first on what kinds of attention to these issues were apparent in the database, and second on what kinds of results were produced. Some of the studies used multiple methods to provide readers with information on these issues. In our report on the evaluations, we both provide descriptive information on the approaches used and summarize the results of those studies. Developing more effective methods to monitor the achievement of these objectives may need to go beyond what is reported in this study.

Among the 63 at least minimally methodologically adequate studies, 26 reported on the effects of their programs on subgroups of students. The

TABLE 5-13 Most Common Subgroups Used in the Analyses and the Number of Studies That Reported on That Variable

other 37 reported on the effects of the curricular intervention on means of whole groups and their standard deviations, but did not report on their data in terms of the impact on subpopulations. Of those 26 evaluations, 19 studies were on NSF-supported programs and 7 were on commercially generated materials. Table 5-13 reports the most common subgroups used in the analyses and the number of studies that reported on that variable. Because many studies used multiple categories for disaggregation (ethnicity, SES, and gender), the number of reports is more than double the number of studies. For this reason, we report the study results in terms of the “frequency of reports on a particular subgroup” and distinguish this from what we refer to as “study counts.” The advantage of this approach is that it permits reporting on studies that investigated multiple ways to disaggregate their data. The disadvantage is that in a sense, studies undertaking multiple disaggregations become overrepresented in the data set as a result. A similar distinction and approach were used in our treatment of disaggregation by content strands.

It is apparent from these data that the evaluators of NSF-supported curricula documented more equity-based outcomes, as they reported 43 of the 56 comparisons. However, the same percentage of the NSF-supported evaluations disaggregated their results by subgroup, as did commercially generated evaluations (41 percent in both cases). This is an area where evaluations of curricula could benefit greatly from standardization of ex-

pectation and methodology. Given the importance of the topic of equity, it should be standard practice to include such analyses in evaluation studies.

In summarizing these 26 studies, the first consideration was whether representative samples of students were evaluated. As we have learned from medical studies, if conclusions on effectiveness are drawn without careful attention to representativeness of the sample relative to the whole population, then the generalizations drawn from the results can be seriously flawed. In Chapter 2 we reported that across the studies, approximately 81 percent of the comparative studies and 73 percent of the case studies reported data on school location (urban, suburban, rural, or state/region), with suburban students being the largest percentage in both study types. The proportions of students studied indicated a tendency to undersample urban and rural populations and oversample suburban schools. With a high concentration of minorities and lower SES students in these areas, there are some concerns about the representativeness of the work.

A second consideration was to see whether the achievement effects of curricular interventions were achieved evenly among the various subgroups. Studies answered this question in different ways. Most commonly, evaluators reported on the performance of various subgroups in the treatment conditions as compared to those same subgroups in the comparative condition. They reported outcome scores or gains from pretest to posttest. We refer to these as “between” comparisons.

Other studies reported on the differences among subgroups within an experimental treatment, describing how well one group does in comparison with another group. Again, these reports were done in relation either to outcome measures or to gains from pretest to posttest. Often these reports contained a time element, reporting on how the internal achievement patterns changed over time as a curricular program was used. We refer to these as “within” comparisons.

Some studies reported both between and within comparisons. Others did not report findings by comparing mean scores or gains, but rather created regression equations that predicted the outcomes and examined whether demographic characteristics are related to performance. Six studies (all on NSF-supported curricula) used this approach with variables related to subpopulations. Twelve studies used ANCOVA or Multiple Analysis of Variance (MANOVA) to study disaggregation by subgroup, and two reported on comparative effect sizes. In the studies using statistical tests other than t-tests or Chi-squares, two were evaluations of commercially generated materials and the rest were of NSF-supported materials.

Of the studies that reported on gender (n=19), the NSF-supported ones (n=13) reported five cases in which the females outperformed their counterparts in the controls and one case in which the female-male gap decreased within the experimental treatments across grades. In most cases, the studies

present a mixed picture with some bright spots, with the majority showing no significant difference. One study reported significant improvements for African-American females.

In relation to race, 15 of 16 reports on African Americans showed positive effects in favor of the treatment group for NSF-supported curricula. Two studies reported decreases in the gaps between African Americans and whites or Asians. One of the two evaluations of African Americans, performance reported for the commercially generated materials, showed significant positive results, as mentioned previously.

For Hispanic students, 12 of 15 reports of the NSF-supported materials were significantly positive, with the other 3 showing no significant difference. One study reported a decrease in the gaps in favor of the experimental group. No evaluations of commercially generated materials were reported on Hispanic populations. Other reports on ethnic groups occurred too seldom to generalize.

Students from lower socioeconomic groups fared well, according to reported evaluations of NSF-supported materials (n=8), in that experimental groups outperformed control groups in all but one case. The one study of commercially generated materials that included SES as a variable reported no significant difference. For students with limited English proficiency, of the two evaluations of NSF-supported materials, one reported significantly more positive results for the experimental treatment. Likewise, one study of commercially generated materials yielded a positive result at the elementary level.

We also examined the data for ability differences and found reports by quartiles for a few evaluation studies. In these cases, the evaluations showed results across quartiles in favor of the NSF-supported materials. In one case using the same program, the lower quartiles showed the most improvement, and in the other, the gains were in the middle and upper groups for the Iowa Test of Basic Skills and evenly distributed for the informal assessment.

Summary Statements

After reviewing these studies, the committee observed that examining differences by gender, race, SES, and performance levels should be examined as a regular part of any review of effectiveness. We would recommend that all comparative studies report on both “between” and “within” comparisons so that the audience of an evaluation can simply and easily consider the level of improvement, its distribution across subgroups, and the impact of curricular implementation on any gaps in performance. Each of the major categories—gender, race/ethnicity, SES, and achievement level—contributes a significant and contrasting view of curricular impact. Further-

more, more sophisticated accounts would begin to permit, across studies, finer distinctions to emerge, such as the effect of a program on young African-American women or on first generation Asian students.

In addition, the committee encourages further study and deliberation on the use of more complex approaches to the examination of equity issues. This is particularly important due to the overlaps among these categories, where poverty can show itself as its own variable but also may be highly correlated to prior performance. Hence, the use of one variable can mask differences that should be more directly attributable to another. The committee recommends that a group of measurement and equity specialists confer on the most effective design to advance on these questions.

Finally, it is imperative that evaluation studies systematically include demographically representative student populations and distinguish evaluations that follow the commercial patterns of use from those that seek to establish effectiveness with a diverse student population. Along these lines, it is also important that studies report on the impact data on all substantial ethnic groups, including whites. Many studies, perhaps because whites were the majority population, failed to report on this ethnic group in their analyses. As we saw in one study, where Asian students were from poor homes and first generation, any subgroup can be an at-risk population in some setting, and because gains in means may not necessarily be assumed to translate to gains for all subgroups or necessarily for the majority subgroup. More complete and thorough descriptions and configurations of characteristics of the subgroups being served at any location—with careful attention to interactions—is needed in evaluations.

Interactions Among Content and Equity, by Grade Band

By examining disaggregation by content strand by grade levels, along with disaggregation by diverse subpopulations, the committee began to discover grade band patterns of performance that should be useful in the conduct of future evaluations. Examining each of these issues in isolation can mask some of the overall effects of curricular use. Two examples of such analysis are provided. The first example examines all the evaluations of NSF-supported curricula from the elementary level. The second examines the set of evaluations of NSF-supported curricula at the high school level, and cannot be carried out on evaluations of commercially generated programs because they lack disaggregation by student subgroup.

Example One

At the elementary level, the findings of the review of evaluations of data on effectiveness of NSF-supported curricula report consistent patterns of

benefits to students. Across the studies, it appears that positive results are enhanced when accompanied by adequate professional development and the use of pedagogical methods consistent with those indicated by the curricula. The benefits are most consistently evidenced in the broadening topics of geometry, measurement, probability, and statistics, and in applied problem solving and reasoning. It is important to consider whether the outcome measures in these areas demonstrate a depth of understanding. In early understanding of fractions and algebra, there is some evidence of improvement. Weaknesses are sometimes reported in the areas of computational skills, especially in the routinization of multiplication and division. These assertions are tentative due to the possible flaws in designs but quite consistent across studies, and future evaluations should seek to replicate, modify, or discredit these results.

The way to most efficiently and effectively link informal reasoning and formal algorithms and procedures is an open question. Further research is needed to determine how to most effectively link the gains and flexibility associated with student-generated reasoning to the automaticity and generalizability often associated with mastery of standard algorithms.

The data from these evaluations at the elementary level generally present credible evidence of increased success in engaging minority students and students in poverty based on reported gains that are modestly higher for these students than for the comparative groups. What is less well documented in the studies is the extent to which the curricula counteract the tendencies to see gaps emerge and result in long-term persistence in performance by gender and minority group membership as they move up the grades. However, the evaluations do indicate that these curricula can help, and almost never do harm. Finally, on the question of adequate challenge for advanced and talented students, the data are equivocal. More attention to this issue is needed.

Example Two

The data at the high school level produced the most conflicting results, and in conducting future evaluations, evaluators will need to examine this level more closely. We identify the high school as the crucible for curricular change for three reasons: (1) the transition to postsecondary education puts considerable pressure on these curricula; (2) the criteria outlined in the NSF RFP specify significant changes from traditional practice; and (3) high school freshmen arrive from a myriad of middle school curricular experiences. For the NSF-supported curricula, the RFP required that the programs provide a core curriculum “drawn from statistics/probability, algebra/functions, geometry/trigonometry, and discrete mathematics” (NSF, 1991, p. 2) and use “a full range of tools, including graphing calculators

and computers” (NSF, 1991, p. 2). The NSF RFP also specified the inclusion of “situations from the natural and social sciences and from other parts of the school curriculum as contexts for developing and using mathematics” (NSF, 1991, p. 1). It was during the fourth year that “course options should focus on special mathematical needs of individual students, accommodating not only the curricular demands of the college-bound but also specialized applications supportive of the workplace aspirations of employment-bound students” (NSF, 1991, p. 2). Because this set of requirements comprises a significant departure from conventional practice, the implementation of the high school curricula should be studied in particular detail.

We report on a Systemic Initiative for Montana Mathematics and Science (SIMMS) study by Souhrada (2001) and Brown et al. (1990), in which students were permitted to select traditional, reform, and mixed tracks. It became apparent that the students were quite aware of the choices they faced, as illustrated in the following quote:

The advantage of the traditional courses is that you learn—just math. It’s not applied. You get a lot of math. You may not know where to use it, but you learn a lot…. An advantage in SIMMS is that the kids in SIMMS tell me that they really understand the math. They understand where it comes from and where it is used.

This quote succinctly captures the tensions reported as experienced by students. It suggests that student perceptions are an important source of evidence in conducting evaluations. As we examined these curricular evaluations across the grades, we paid particular attention to the specificity of the outcome measures in relation to curricular objectives. Overall, a review of these studies would lead one to draw the following tentative summary conclusions:

There is some evidence of discontinuity in the articulation between high school and college, resulting from the organization and emphasis of the new curricula. This discontinuity can emerge in scores on college admission tests, placement tests, and first semester grades where nonreform students have shown some advantage on typical college achievement measures.

The most significant areas of disadvantage seem to be in students’ facility with algebraic manipulation, and with formalization, mathematical structure, and proof when isolated from context and denied technological supports. There is some evidence of weakness in computation and numeration, perhaps due to reliance on calculators and varied policies regarding their use at colleges (Kahan, 1999; Huntley et al., 2000).

There is also consistent evidence that the new curricula present

strengths in areas of solving applied problems, the use of technology, new areas of content development such as probability and statistics and functions-based reasoning in the use of graphs, using data in tables, and producing equations to describe situations (Huntley et al., 2000; Hirsch and Schoen, 2002).

Despite early performance on standard outcome measures at the high school level showing equivalent or better performance by reform students (Austin et al., 1997; Merlino and Wolff, 2001), the common standardized outcome measures (Preliminary Scholastic Assessment Test [PSAT] scores or national tests) are too imprecise to determine with more specificity the comparisons between the NSF-supported and comparison approaches, while program-generated measures lack evidence of external validity and objectivity. There is an urgent need for a set of measures that would provide detailed information on specific concepts and conceptual development over time and may require use as embedded as well as summative assessment tools to provide precise enough data on curricular effectiveness.

The data also report some progress in strengthening the performance of underrepresented groups in mathematics relative to their counterparts in the comparative programs (Schoen et al., 1998; Hirsch and Schoen, 2002).

This reported pattern of results should be viewed as very tentative, as there are only a few studies in each of these areas, and most do not adequately control for competing factors, such as the nature of the course received in college. Difficulties in the transition may also be the result of a lack of alignment of measures, especially as placement exams often emphasize algebraic proficiencies. These results are presented only for the purpose of stimulating further evaluation efforts. They further emphasize the need to be certain that such designs examine the level of mathematical reasoning of students, particularly in relation to their knowledge of understanding of the role of proofs and definitions and their facility with algebraic manipulation as we as carefully document the competencies taught in the curricular materials. In our framework, gauging the ease of transition to college study is an issue of examining curricular alignment with systemic factors, and needs to be considered along with those tests that demonstrate a curricular validity of measures. Furthermore, the results raising concerns about college success need replication before secure conclusions are drawn.

Also, it is important that subsequent evaluations also examine curricular effects on students’ interest in mathematics and willingness to persist in its study. Walker (1999) reported that there may be some systematic differences in these behaviors among different curricula and that interest and persistence may help students across a variety of subgroups to survive entry-level hurdles, especially if technical facility with symbol manipulation

can be improved. In the context of declines in advanced study in mathematics by American students (Hawkins, 2003), evaluation of curricular impact on students’ interest, beliefs, persistence, and success are needed.

The committee takes the position that ultimately the question of the impact of different curricula on performance at the collegiate level should be resolved by whether students are adequately prepared to pursue careers in mathematical sciences, broadly defined, and to reason quantitatively about societal and technological issues. It would be a mistake to focus evaluation efforts solely or primarily on performance on entry-level courses, which can clearly function as filters and may overly emphasize procedural competence, but do not necessarily represent what concepts and skills lead to excellence and success in the field.

These tentative patterns of findings indicate that at the high school level, it is necessary to conduct individual evaluations that examine the transition to college carefully in order to gauge the level of success in preparing students for college entry and the successful negotiation of majors. Equally, it is imperative to examine the impact of high school curricula on other possible student trajectories, such as obtaining high school diplomas, moving into worlds of work or through transitional programs leading to technical training, two-year colleges, and so on.

These two analyses of programs by grade-level band, content strand, and equity represent a methodological innovation that could strengthen the empirical database on curricula significantly and provide the level of detail really needed by curriculum designers to improve their programs. In addition, it appears that one could characterize the NSF programs (and not the commercial programs as a group) as representing a particular approach to curriculum, as discussed in Chapter 3 . It is an approach that integrates content strands; relies heavily on the use of situations, applications, and modeling; encourages the use of technology; and has a significant dose of mathematical inquiry. One could ask the question of whether this approach as a whole is “effective.” It is beyond the charge and scope of this report, but is a worthy target of investigation if one uses proper care in design, execution, and analysis. Likewise other approaches to curricular change should be investigated at the aggregate level, using careful and rigorous design.

The committee believes that a diversity of curricular approaches is a strength in an educational system that maintains local and state control of curricular decision making. While “scientifically established as effective” should be an increasingly important consideration in curricular choice, local cultural differences, needs, values, and goals will also properly influence curricular choice. A diverse set of effective curricula would be ideal. Finally, the committee emphasizes once again the importance of basing the studies on measures with established curricular validity and avoiding cor-

ruption of indicators as a result of inappropriate amounts of teaching to the test, so as to be certain that the outcomes are the product of genuine student learning.

CONCLUSIONS FROM THE COMPARATIVE STUDIES

In summary, the committee reviewed a total of 95 comparative studies. There were more NSF-supported program evaluations than commercial ones, and the commercial ones were primarily on Saxon or UCSMP materials. Of the 19 curricular programs reviewed, 23 percent of the NSF-supported and 33 percent of the commercially generated materials selected had programs with no comparative reviews. This finding is particularly disturbing in light of the legislative mandate in No Child Left Behind (U.S. Department of Education, 2001) for scientifically based curricular programs and materials to be used in the schools. It suggests that more explicit protocols for the conduct of evaluation of programs that include comparative studies need to be required and utilized.

Sixty-nine percent of NSF-supported and 61 percent of commercially generated program evaluations met basic conditions to be classified as at least minimally methodologically adequate studies for the evaluation of effectiveness. These studies were ones that met the criteria of including measures of student outcomes on mathematical achievement, reporting a method of establishing comparability among samples and reporting on implementation elements, disaggregating by content strand, or using precise, theoretical analyses of the construct or multiple measures.

Most of these studies had both strengths and weaknesses in their quasi-experimental designs. The committee reviewed the studies and found that evaluators had developed a number of features that merit inclusions in future work. At the same time, many had internal threats to validity that suggest a need for clearer guidelines for the conduct of comparative evaluations.

Many of the strengths and innovations came from the evaluators’ understanding of the program theories behind the curricula, their knowledge of the complexity of practice, and their commitment to measuring valid and significant mathematical ideas. Many of the weaknesses came from inadequate attention to experimental design, insufficient evidence of the independence of evaluators in some studies, and instability and lack of cooperation in interfacing with the conditions of everyday practice.

The committee identified 10 elements of comparative studies needed to establish a basis for determining the effectiveness of a curriculum. We recognize that not all studies will be able to implement successfully all elements, and those experimental design variations will be based largely on study size and location. The list of elements begins with the seven elements

corresponding to the seven critical decisions and adds three additional elements that emerged as a result of our review:

A better balance needs to be achieved between experimental and quasi-experimental studies. The virtual absence of large-scale experimental studies does not provide a way to determine whether the use of quasi-experimental approaches is being systematically biased in unseen ways.

If a quasi-experimental design is selected, it is necessary to establish comparability. When quasi-experimentation is used, it “pertains to studies in which the model to describe effects of secondary variables is not known but assumed” (NRC, 1992, p. 18). This will lead to weaker and potentially suspect causal claims, which should be acknowledged in the evaluation report, but may be necessary in relation to feasibility (Joint Committee on Standards for Educational Evaluation, 1994). In general, to date, studies have assumed prior achievement measures, ethnicity, gender, and SES, are acceptable variables on which to match samples or on which to make statistical adjustments. But there are often other variables in need of such control in such evaluations including opportunity to learn, teacher effectiveness, and implementation (see #4 below).

The selection of a unit of analysis is of critical importance to the design. To the extent possible, it is useful to randomly assign the unit for the different curricula. The number of units of analysis necessary for the study to establish statistical significance depends not on the number of students, but on this unit of analysis. It appears that classrooms and schools are the most likely units of analysis. In addition, the development of increasingly sophisticated means of conducting studies that recognize that the level of the educational system in which experimentation occurs affects research designs.

It is essential to examine the implementation components through a set of variables that include the extent to which the materials are implemented, teaching methods, the use of supplemental materials, professional development resources, teacher background variables, and teacher effects. Gathering these data to gauge the level of implementation fidelity is essential for evaluators to ensure adequate implementation. Studies could also include nested designs to support analysis of variation by implementation components.

Outcome data should include a variety of measures of the highest quality. These measures should vary by question type (open ended, multiple choice), by type of test (international, national, local) and by relation of testing to everyday practice (formative, summative, high stakes), and ensure curricular validity of measures and assess curricular alignment with systemic factors. The use of comparisons among total tests, fair tests, and

conservative tests, as done in the evaluations of UCSMP, permits one to gain insight into teacher effects and to contrast test results by items included. Tests should also include content strands to aid disaggregation, at a level of major content strands (see Figure 5-11 ) and content-specific items relevant to the experimental curricula.

Statistical analysis should be conducted on the appropriate unit of analysis and should include more sophisticated methods of analysis such as ANOVA, ANCOVA, MACOVA, linear regression, and multiple regression analysis as appropriate.

Reports should include clear statements of the limitations to generalization of the study. These should include indications of limitations in populations sampled, sample size, unique population inclusions or exclusions, and levels of use or attrition. Data should also be disaggregated by gender, race/ethnicity, SES, and performance levels to permit readers to see comparative gains across subgroups both between and within studies.

It is useful to report effect sizes. It is also useful to present item-level data across treatment program and show when performances between the two groups are within the 10 percent confidence interval of each other. These two extremes document how crucial it is for curricula developers to garner both precise and generalizable information to inform their revisions.

Careful attention should also be given to the selection of samples of populations for participation. These samples should be representative of the populations to whom one wants to generalize the results. Studies should be clear if they are generalizing to groups who have already selected the materials (prior users) or to populations who might be interested in using the materials (demographically representative).

The control group should use an identified comparative curriculum or curricula to avoid comparisons to unstructured instruction.

In addition to these prototypical decisions to be made in the conduct of comparative studies, the committee suggests that it would be ideal for future studies to consider some of the overall effects of these curricula and to test more directly and rigorously some of the findings and alternative hypotheses. Toward this end, the committee reported the tentative findings of these studies by program type. Although these results are subject to revision, based on the potential weaknesses in design of many of the studies summarized, the form of analysis demonstrated in this chapter provides clear guidance about the kinds of knowledge claims and the level of detail that we need to be able to judge effectiveness. Until we are able to achieve an array of comparative studies that provide valid and reliable information on these issues, we will be vulnerable to decision making based excessively on opinion, limited experience, and preconceptions.

This book reviews the evaluation research literature that has accumulated around 19 K-12 mathematics curricula and breaks new ground in framing an ambitious and rigorous approach to curriculum evaluation that has relevance beyond mathematics. The committee that produced this book consisted of mathematicians, mathematics educators, and methodologists who began with the following charge:

• Evaluate the quality of the evaluations of the thirteen National Science Foundation (NSF)-supported and six commercially generated mathematics curriculum materials;
• Determine whether the available data are sufficient for evaluating the efficacy of these materials, and if not;
• Develop recommendations about the design of a project that could result in the generation of more reliable and valid data for evaluating such materials.

The committee collected, reviewed, and classified almost 700 studies, solicited expert testimony during two workshops, developed an evaluation framework, established dimensions/criteria for three methodologies (content analyses, comparative studies, and case studies), drew conclusions on the corpus of studies, and made recommendations for future research.

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Comparative Case Studies: Methodological Discussion

• Open Access
• First Online: 25 May 2022

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• Marcelo Parreira do Amaral 7  

Part of the book series: Palgrave Studies in Adult Education and Lifelong Learning ((PSAELL))

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Case Study Research has a long tradition and it has been used in different areas of social sciences to approach research questions that command context sensitiveness and attention to complexity while tapping on multiple sources. Comparative Case Studies have been suggested as providing effective tools to understanding policy and practice along three different axes of social scientific research, namely horizontal (spaces), vertical (scales), and transversal (time). The chapter, first, sketches the methodological basis of case-based research in comparative studies as a point of departure, also highlighting the requirements for comparative research. Second, the chapter focuses on presenting and discussing recent developments in scholarship to provide insights on how comparative researchers, especially those investigating educational policy and practice in the context of globalization and internationalization, have suggested some critical rethinking of case study research to account more effectively for recent conceptual shifts in the social sciences related to culture, context, space and comparison. In a third section, it presents the approach to comparative case studies adopted in the European research project YOUNG_ADULLLT that has set out to research lifelong learning policies in their embeddedness in regional economies, labour markets and individual life projects of young adults. The chapter is rounded out with some summarizing and concluding remarks.

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Introduction to the Book and the Comparative Study

Comparative Studies, the Experience of COMPALL Winter School

Theoretical and Methodological Considerations

• Case-based research
• Comparative case studies

1 Introduction

Exploring landscapes of lifelong learning in Europe is a daunting task as it involves a great deal of differences across places and spaces; it entails attending to different levels and dimensions of the phenomena at hand, but not least it commands substantial sensibility to cultural and contextual idiosyncrasies. As such, case-based methodologies come to mind as tested methodological approaches to capturing and examining singular configurations such as the local settings in focus in this volume, in which lifelong learning policies for young people are explored in their multidimensional reality. The ensuing question, then, is how to ensure comparability across cases when departing from the assumption that cases are unique. Recent debates in Comparative and International Education (CIE) research are drawn from that offer important insights into the issues involved and provide a heuristic approach to comparative cases studies. Since the cases focused on in the chapters of this book all stem from a common European research project, the comparative case study methodology allows us to at once dive into the specifics and uniqueness of each case while at the same time pay attention to common treads at the national and international (European) levels.

The chapter, first, sketches the methodological basis of case-based research in comparative studies as a point of departure, also highlighting the requirements in comparative research. In what follows, second, the chapter focuses on presenting and discussing recent developments in scholarship to provide insights on how comparative researchers, especially those investigating educational policy and practice in the context of globalization and internationalization, have suggested some critical rethinking of case study research to account more effectively for recent conceptual shifts in the social sciences related to culture, context, space and comparison. In a third section, it presents the approach to comparative case studies adopted in the European research project YOUNG_ADULLLT that has set out to research lifelong learning policies in their embeddedness in regional economies, labour markets and individual life projects of young adults. The chapter is rounded out with some summarizing and concluding remarks.

2 Case-Based Research in Comparative Studies

In the past, comparativists have oftentimes regarded case study research as an alternative to comparative studies proper. At the risk of oversimplification: methodological choices in comparative and international education (CIE) research, from the 1960s onwards, have fallen primarily on either single country (small n) contextualized comparison, or on cross-national (usually large n, variable) decontextualized comparison (see Steiner-Khamsi, 2006a , 2006b , 2009). These two strands of research—notably characterized by Development and Area Studies on the one side and large-scale performance surveys of the International Association for the Evaluation of Educational Achievement (IEA) type, on the other—demarcated their fields by resorting to how context and culture were accounted for and dealt with in the studies they produced. Since the turn of the century, though, comparativists are more comfortable with case study methodology (see Little, 2000 ; Vavrus and Bartlett 2006 , 2009 ; Bartlett & Vavrus, 2017 ) and diagnoses of an “identity crisis” of the field due to a mass of single-country studies lacking comparison proper (see Schriewer, 1990 ; Wiseman & Anderson, 2013 ) started dying away. Greater acceptance of and reliance on case-based methodology has been related with research on policy and practice in the context of globalization and coupled with the intention to better account for culture and context, generating scholarship that is critical of power structures, sensitive to alterity and of other ways of knowing.

The phenomena that have been coined as constituting “globalization” and “internationalization” have played, as mentioned, a central role in the critical rethinking of case study research. In researching education under conditions of globalization, scholars placed increasing attention on case-based approaches as opportunities for investigating the contemporary complexity of policy and practice. Further, scholarly debates in the social sciences and the humanities surrounding key concepts such as culture, context, space, and place but also comparison have also contributed to a reconceptualization of case study methodology in CIE. In terms of the requirements for such an investigation, scholarship commands an adequate conceptualization that problematizes the objects of study and that does not take them as “unproblematic”, “assum[ing] a constant shared meaning”; in short, objects of study that are “fixed, abstract and absolute” (Fine, quoted in Dale & Robertson, 2009 , p. 1114). Case study research is thus required to overcome methodological “isms” in their research conceptualization (see Dale & Robertson, 2009 ; Robertson & Dale, 2017 ; see also Lange & Parreira do Amaral, 2018 ). In response to these requirements, the approaches to case study discussed in CIE depart from a conceptualization of the social world as always dynamic, emergent, somewhat in motion, and always contested. This view considers the fact that the social world is culturally produced and is never complete or at a standstill, which goes against an understanding of case as something fixed or natural. Indeed, in the past cases have often been understood almost in naturalistic ways, as if they existed out there, waiting for researchers to “discover” them. Usually, definitions of case study also referred to inquiry that aims at elucidating features of a phenomenon to yield an understanding of why, how and with what consequences something happens. One can easily find examples of cases understood simply as sites to observe/measure variables—in a nomothetic cast—or examples, where cases are viewed as specific and unique instances that can be examined in the idiographic paradigm. In contrast, rather than taking cases as pre-existing entities that are defined and selected as cases, recent case-oriented research has argued for a more emergent approach which recognizes that boundaries between phenomenon and context are often difficult to establish or overlap. For this reason, researchers are incited to see this as an exercise of “casing”, that is, of case construction. In this sense, cases here are seen as complex systems (Ragin & Becker, 1992 ) and attention is devoted to the relationships between the parts and the whole, pointing to the relevance of configurations and constellations within as well as across cases in the explanation of complex and contingent phenomena. This is particularly relevant for multi-case, comparative research since the constitution of the phenomena that will be defined, as cases will differ. Setting boundaries will thus also require researchers to account for spatial, scalar (i.e., level or levels with which a case is related) and temporal aspects.

Further, case-based research is also required to account for multiple contexts while not taking them for granted. One of the key theoretical and methodological consequences of globalization for CIE is that it required us to recognize that it alters the nature and significance of what counts as contexts (see Parreira do Amaral, 2014 ). According to Dale ( 2015 ), designating a process, or a type of event, or a particular organization, as a context, entails bestowing a particular significance on them, as processes, events, and so on that are capable of affecting other processes and events. The key point is that rather than being so intrinsically, or naturally, contexts are constructed as “contexts”. In comparative research, contexts have been typically seen as the place (or the variables) that enable us to explain why what happens in one case is different from what happens another case; what counts as context then is seen as having the same effect everywhere, although the forms it takes vary substantially (see Dale, 2015 ). In more general terms, recent case study approaches aim at accounting for the increasing complexity of the contexts in which they are embedded, which, in turn, is related to the increasing impact of globalization as the “context of contexts” (Dale, 2015 , p. 181f; see also Carter & Sealey, 2013 ; Mjoset, 2013 ). It also aims at accounting for overlapping contexts. Here it is important to note that contexts are not only to be seen in spatio-geographical terms (i.e., local, regional, national, international), but contexts may also be provided by different institutional and/or discursive contexts that create varying opportunity structures (Dale & Parreira do Amaral, 2015 ; see also Chap. 2 in this volume). What one can call temporal contexts also plays an important role, for what happens in the case unfolds as embedded not only in historical time, but may be related to different temporalities (see the concept of “timespace” as discussed by Lingard & Thompson, 2016 ) and thus are influenced by path dependence or by specific moments of crisis (Rhinard, 2019 ; see also McLeod, 2016 ). Moreover, in CIE research, the social-cultural production of the world is influenced by developments throughout the globe that take place at various places and on several scales, which in turn influence each other, but in the end, become locally relevant in different facets. As Bartlett and Vavrus write, “context is not a primordial or autonomous place; it is constituted by social interactions, political processes, and economic developments across scales and times.” ( Bartlett & Vavrus, 2017 , p. 14). Indeed, in this sense, “context is not a container for activity, it is the activity” (Bartlett & Vavrus, 2017 , p. 12, emphasis in orig.).

Also, dealing with the complexity of education policy and practice requires us to transcend the dichotomy of idiographic versus nomothetic approaches to causation. Here, it can be argued that case studies allow us to grasp and research the complexity of the world, thus offering conceptual and methodological tools to explore how phenomena viewed as cases “depend on all of the whole, the parts, the interactions among parts and whole, and the interactions of any system with other complex systems among which it is nested and with which it intersects” (Byrne, 2013 , p. 2). The understanding of causation that undergirds recent developments in case-based research aims at generalization, yet it resists ambitions to establishing universal laws in social scientific research. Focus is placed on processes while tracking the relevant factors, actors and features that help explain the “how” and the “why” questions (Bartlett and Vavrus 2017 , p. 38ff), and on “causal mechanisms”, as varying explanations of outcomes within and across cases, always contingent on interaction with other variables and dependent contexts (see Byrne, 2013 ; Ragin, 2000 ). In short, the nature of causation underlying the recent case study approaches in CIE is configurational and not foundational.

This is also in line with how CIE research regards education practice, research, and policy as a socio-cultural practice. And it refers to the production of social and cultural worlds through “social actors, with diverse motives, intentions, and levels of influence, [who] work in tandem with and/or in response to social forces” (Bartlett and Vavrus 2017 , p. 1). From this perspective, educational phenomena, such as in policymaking, are seen as a “deeply political process of cultural production engaged in and shaped by social actors in disparate locations who exert incongruent amounts of influence over the design, implementation, and evaluation of policy” ( Bartlett & Vavrus, 2017 , p. 1f). Culture here is understood in non-static and complex ways that reinforce the “importance of examining processes of sense-making as they develop over time, in distinct settings, in relation to systems of power and inequality, and in increasingly interconnected conversation with actors who do not sit physically within the circle drawn around the traditional case” (Bartlett & Vavrus, 2017 , p. 11, emphasis in orig.).

In sum, the approaches to case study put forward in CIE provide conceptual and methodological tools that allow for an analysis of education in the global context throughout scale, space, and time, which is always regarded as complexly integrated and never as isolated or independent. The following subsection discusses Comparative Case Studies (CCS) as suggested in recent comparative scholarship, which aims at attending to the methodological requirements discussed above by integrating horizontal, vertical, and transversal dimensions of comparison.

2.1 Comparative Case Studies: Horizontal, Vertical and Transversal Dimensions

Building up on their previous work on vertical case studies (Bartlett and Vavrus 2017 ; Vavrus & Bartlett, 2006 , 2009 ), Frances Vavrus and Lesley Bartlett have proposed a comparative approach to case study research that aims at meeting the requirements of culture and context sensitive research as discussed in this special issue.

As a research approach, CCS offers two theoretical-methodological lenses to research education as a socio-cultural practice. These lenses represent different views on the research object and account for the complexity of education practice, policy, and research in globalized contexts. The first lens is “context-sensitive”, which focuses on how social practices and interactions constitute and produce social contexts. As quoted above, from the perspective of a socio-cultural practice, “context is not a container for activity, it is the activity” (Vavrus and Bartlett 2017: 12, emphasis in orig.). The settings that influence and condition educational phenomena are culturally produced in different and sometimes overlapping (spatial, institutional, discursive, temporal) contexts as just mentioned. The second CCS lens is “culture-sensitive” and focuses on how socio-cultural practices produce social structures. As such, culture is a process that is emergent, dynamic, and constitutive of meaning-making as well as social structuration.

The CCS approach aims at studying educational phenomena throughout scale, time, and space by providing three axes for a “studying through” of the phenomena in question. As stated by Lesley Bartlett and Frances Vavrus with reference to comparative analyses of global education policy:

the horizontal axis compares how similar policies unfold in distinct locations that are socially produced […] and ‘complexly connected’ […]. The vertical axis insists on simultaneous attention to and across scales […]. The transversal comparison historically situates the processes or relations under consideration (Bartlett and Vavrus 2017 : 3, emphasis in orig.).

These three axes allow for a methodological conceptualization of “policy formation and appropriation across micro-, meso-, and macro levels” by not theorizing them as distinct or unrelated (Bartlett and Vavrus 2017 , p. 4). In following Latour, they state:

the macro is neither “above” nor “below” the intersections but added to them as another of their connections’ […]. In CCS research, one would pay close attention to how actions at different scales mutually influence one another (Bartlett and Vavrus 2017 , p. 13f, emphasis in orig.)

Thus, these three axes contain

processes across space and time; and [the CCS as a research design] constantly compares what is happening in one locale with what has happened in other places and historical moments. These forms of comparison are what we call horizontal, vertical, and transversal comparisons (Bartlett and Vavrus 2017 , p. 11, emphasis in orig.)

In terms of the three axes along with comparison is organized, the authors state that horizontal comparison commands attention to how historical and contemporary processes have variously influenced the “cases”, which might be constructed by focusing “people, groups of people, sites, institutions, social movements, partnerships, etc.” (Bartlett and Vavrus 2017 , p. 53) Horizontal comparisons eschew pressing categories resultant from one case others, which implies including multiple cases at the same scale in a comparative case study, while at the same time attending to “valuable contextual information” about each of them. Horizontal comparisons use units of analysis that are homologous, that is, equivalent in terms of shape, function, or institutional/organizational nature (for instance, schools, ministries, countries, etc.) ( Bartlett & Vavrus, 2017 , p. 53f). Similarly, comparative case studies may also entail tracing a phenomenon across sites, as in multi-sited ethnography (see Coleman & von Hellermann, 2012 ; Marcus, 1995 ).

Vertical comparison, in turn, does not simply imply the comparison of levels; rather it involves analysing networks and their interrelationships at different scales. For instance, in the study of policymaking in a specific case, vertical comparison would consider how actors at different scales variably respond to a policy issued at another level—be it inter−/supranational or at the subnational level. CCS assumes that their different appropriation of policy as discourse and as practice is often due to different histories of racial, ethnic, or gender politics in their communities that appropriately complicate the notion of a single cultural group (Bartlett and Vavrus 2017 , p. 73f). Establishing what counts as context in such a study would be done “by tracing the formation and appropriation of a policy” at different scales; and “by tracing the processes by which actors and actants come into relationship with one another and form non-permanent assemblages aimed at producing, implementing, resisting, and appropriating policy to achieve particular aims” ( Bartlett & Vavrus, 2017 , p. 76). A further element here is that, in this way, one may counter the common problem that comparison of cases (oftentimes countries) usually overemphasizes boundaries and treats them as separated or as self-sustaining containers, when, in reality, actors and institutions at other levels/scales significantly impact policymaking (Bartlett & Vavrus, 2017 ).

In terms of the transversal axis of comparison, Bartlett and Vavrus argue that the social phenomena of interest in a case study have to be seen in light of their historical development (Bartlett & Vavrus, 2017 , p. 93), since these “historical roots” impacted on them and “continues to reverberate into the present, affecting economic relations and social issues such as migration and educational opportunities.” As such, understanding what goes on in a case requires to “understand how it came to be in the first place.” ( Bartlett & Vavrus, 2017 , p. 93) argue:

history offers an extensive fount of evidence regarding how social institutions function and how social relations are similar and different around the world. Historical analysis provides an essential opportunity to contrast how things have changed over time and to consider what has remained the same in one locale or across much broader scales. Such historical comparison reveals important insights about the flexible cultural, social, political, and economic systems humans have developed and sustained over time (Bartlett & Vavrus, 2017 , p. 94).

Further, time and space are intimately related and studying the historical development of the social phenomena of interest in a case study “allows us to assess evidence and conflicting interpretations of a phenomenon,” but also to interrogate our own assumptions about them in contemporary times (Bartlett and Vavrus 2017 ), thus analytically sharpening our historical analyses.

As argued by the authors, researching the global dimension of education practice, research or policy aims at a “studying through” of phenomena horizontally, vertically, and transversally. That is, comparative case study builds on an emergent research design and on a strong process orientation that aims at tracing not only “what”, but also “why” and “how” phenomena emerge and evolve. This approach entails “an open-ended, inductive approach to discover what […] meanings and influences are and how they are involved in these events and activities—an inherently processual orientation” (Bartlett and Vavrus 2017 , p. 7, emphasis in orig.).

The emergent research design and process orientation of the CCS relativizes a priori, somewhat static notions of case construction in CIE and emphasizes the idea of a processual “casing”. The process of casing put forward by CCS has to be understood as a dynamic and open-ended embedding of “cased” research phenomena within moments of scale, space, and time that produce varying sets of conditions or configurations.

In terms of comparison, the primary logic is well in line with more sophisticated approaches to comparison that not simply establish relationships between observable facts or pre-existing cases; rather, the comparative logic aims at establishing “relations between sets of relationships”, as argued by Jürgen Schriewer:

[the] specific method of science dissociates comparison from its quasi-natural union with resemblances; the interest in identifying similarities shifts from the level of factual contents to the level of generalizable relationships. […] One of the primary ways of extending their scope, or examining their explanatory power, is the controlled introduction of varying sets of conditions. The logic of relating relationships, which distinguishes the scientific method of comparison, comes close to meeting these requirements by systematically exploring and analysing sociocultural differences with respect to scrutinizing the credibility of theories, models or constructs (Schriewer, 1990 , p. 36).

The notion of establishing relations between sets of relationships allows to treat cases not as homogeneous (thus avoiding a universalizing notion of comparison); it establishes comparability not along similarity but based on conceptual, functional and/or theoretical equivalences and focuses on reconstructing ‘varying sets of conditions’ that are seen as relevant in social scientific explanation and theorizing, and to which then comparative case studies may contribute.

The following section aims presents the adaptation and application of a comparative case study approach in the YOUNG_ADULLLT research project.

3 Exploring Landscapes of Lifelong Learning through Case Studies

This section illustrates the usage of comparative case studies by drawing from research conducted in a European research project upon which the chapters in this volume are based. The project departed from the observation that most current European lifelong learning (LLL) policies have been designed to create economic growth and, at the same time, guarantee social inclusion and argued that, while these objectives are complementary, they are, however, not linearly nor causally related and, due to distinct orientations, different objectives, and temporal horizons, conflicts and ambiguities may arise. The project was designed as a mixed-method comparative study and aimed at results at the national, regional, and local levels, focusing in particular on policies targeting young adults in situations of near social exclusion. Using a multi-level approach with qualitative and quantitative methods, the project conducted, amongst others, local/regional 18 case studies of lifelong learning policies through a multi-method and multi-level design (see Parreira do Amaral et al., 2020 for more information). The localisation of the cases in their contexts was carried out by identifying relevant areas in terms of spatial differentiation and organisation of social and economic relations. The so defined “functional regions” allowed focus on territorial units which played a central role within their areas, not necessarily overlapping with geographical and/or administrative borders. Footnote 1

Two main objectives guided the research: first, to analyse policies and programmes at the regional and local level by identifying policymaking networks that included all social actors involved in shaping, formulating, and implementing LLL policies for young adults; second, to recognize strengths and weaknesses (overlapping, fragmented or unfocused policies and projects), thus identifying different patterns of LLL policymaking at regional level, and investigating their integration with the labour market, education and other social policies. The European research project focused predominantly on the differences between the existing lifelong learning policies in terms of their objectives and orientations and questioned their impact on young adults’ life courses, especially those young adults who find themselves in vulnerable positions. What concerned the researchers primarily was the interaction between local institutional settings, education, labour markets, policymaking landscapes, and informal initiatives that together nurture the processes of lifelong learning. They argued that it is by inquiring into the interplay of these components that the regional and local contexts of lifelong learning policymaking can be better assessed and understood. In this regard, the multi-layered approach covered a wide range of actors and levels and aimed at securing compatibility throughout the different phases and parts of the research.

The multi-level approach adopted aimed at incorporating the different levels from transnational to regional/local to individual, that is, the different places, spaces, and levels with which policies are related. The multi-method design was used to bring together the results from the quantitative, qualitative and policy/document analysis (for a discussion: Parreira do Amaral, 2020 ).

Studying the complex relationships between lifelong learning (LLL) policymaking on the one hand, and young adults’ life courses on the other, requires a carefully established research approach. This task becomes even more challenging in the light of the diverse European countries and their still more complex local and regional structures and institutions. One possible way of designing a research framework able to deal with these circumstances clearly and coherently is to adopt a multi-level or multi-layered approach. This approach recognises multiple levels and patterns of analysis and enables researchers to structure the workflow according to various perspectives. It was this multi-layered approach that the research consortium of YOUNG_ADULLLT adopted and applied in its attempts to better understand policies supporting young people in their life course.

3.1 Constructing Case Studies

In constructing case studies, the project did not apply an instrumental approach focused on the assessment of “what worked (or not)?” Rather, consistently with Bartlett and Vavrus’s proposal (Bartlett & Vavrus, 2017 ), the project decided to “understand policy as a deeply political process of cultural production engaged in and shaped by social actors in disparate locations who exert incongruent amounts of influence over the design, implementation, and evaluation of policy” ( Bartlett & Vavrus, 2017 , p. 1f). This was done in order to enhance the interactive and relational dimension among actors and levels, as well as their embeddedness in local infra-structures (education, labour, social/youth policies) according to project’s three theoretical perspectives. The analyses of the information and data integrated by our case study approach aimed at a cross-reading of the relations among the macro socio-economic dimensions, structural arrangements, governance patterns, addressee biographies and mainstream discourses that underlie the process of design and implementation of the LLL policies selected as case study. The subjective dimensions of agency and sense-making animated these analyses, and the multi-level approach contextualized them from the local to the transnational levels. Figure 3.1 below represents the analytical approach to the research material gathered in constructing the case studies. Specifically, it shows the different levels, from the transnational level down to the addressees.

Multi-level and multi-method approach to case studies in YOUNG_ADULLLT. Source: Palumbo et al., 2019

The project partners aimed at a cross-dimensional construction of the case studies, and this implied the possibility of different entry points, for instance by moving the analytical perspective top-down or bottom-up, as well as shifting from left to right of the matrix and vice versa. Considering the “horizontal movement”, the multidimensional approach has enabled taking into consideration the mutual influence and relations among the institutional, individual, and structural dimensions (which in the project corresponded to the theoretical frames of CPE, LCR, and GOV). In addition, the “vertical movement” from the transnational to the individual level and vice versa was meant to carefully carry out a “study of flows of influence, ideas, and actions through these levels” (Bartlett and Vavrus 2017 , p. 11), emphasizing the correspondences/divergences among the perspectives of different actors at different levels. The transversal dimension, that is, the historical process, focused on the period after the financial crisis of 2007/2008 as it has impacted differently on the social and economic situations of young people, often resulting in stern conditions and higher competition in education and labour markets, which also called for a reassessment of existing policies targeting young adults in the countries studied.

Concerning the analyses, a further step included the translation of the conceptual model illustrated in Fig. 3.1 above into a heuristic table used to systematically organize the empirical data collected and guide the analyses cases constructed as multi-level and multidimensional phenomena, allowing for the establishment of interlinkages and relationships. By this approach, the analysis had the possibility of grasping the various levels at which LLL policies are negotiated and displaying the interplay of macro-structures, regional environments and institutions/organizations as well as individual expectations. Table 3.1 illustrates the operationalization of the data matrix that guided the work.

In order to ensure the presentability and intelligibility of the results, Footnote 2 a narrative approach to case studies analysis was chosen whose main task was one of “storytelling” aimed at highlighting what made each case unique and what difference it makes for LLL policymaking and to young people’s life courses. A crucial element of this entails establishing relations “between sets of relationships”, as argued above.

LLL policies were selected as starting points from which the cases themselves could be constructed and of which different stories could be developed. That stories can be told differently does not mean that they are arbitrary, rather this refers to different ways of accounting for the embedding of the specific case to its context, namely the “diverging policy frameworks, patterns of policymaking, networks of implementation, political discourses and macro-structural conditions at local level” (see Palumbo et al., 2020 , p. 220). Moreover, developing different narratives aimed at representing the various voices of the actors involved in the process—from policy-design and appropriation through to implementation—and making the different stakeholders’ and addressees’ opinions visible, creating thus intelligible narratives for the cases (see Palumbo et al., 2020 ). Analysing each case started from an entry point selected, from which a story was told. Mainly, two entry points were used: on the one hand, departing from the transversal dimension of the case and which focused on the evolution of a policy in terms of its main objectives, target groups, governance patterns and so on in order to highlight the intended and unintended effects of the “current version” of the policy within its context and according to the opinions of the actors interviewed. On the other hand, biographies were selected as starting points in an attempt to contextualize the life stories within the biographical constellations in which the young people came across the measure, the access procedures, and how their life trajectories continued in and possibly after their participation in the policy (see Palumbo et al., 2020 for examples of these narrative strategies).

4 Concluding Remarks

This chapter presented and discussed the methodological basis and requirements of conducting case studies in comparative research, such as those presented in the subsequent chapters of this volume. The Comparative Case Study approach suggested in the previous discussion offers productive and innovative ways to account sensitively to culture and contexts; it provides a useful heuristic that deals effectively with issues related to case construction, namely an emergent and dynamic approach to casing, instead of simply assuming “bounded”, pre-defined cases as the object of research; they also offer a helpful procedural, configurational approach to “causality”; and, not least, a resourceful approach to comparison that allows researchers to respect the uniqueness and integrity of each case while at the same time yielding insights and results that transcend the idiosyncrasy of the single case. In sum, CCS offers a sound approach to CIE research that is culture and context sensitive.

For a discussion of the concept of functional region, see Parreira do Amaral et al., 2020 .

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do Amaral, M.P. (2022). Comparative Case Studies: Methodological Discussion. In: Benasso, S., Bouillet, D., Neves, T., Parreira do Amaral, M. (eds) Landscapes of Lifelong Learning Policies across Europe. Palgrave Studies in Adult Education and Lifelong Learning. Palgrave Macmillan, Cham. https://doi.org/10.1007/978-3-030-96454-2_3

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Comparison in Scientific Research: Uncovering statistically significant relationships

by Anthony Carpi, Ph.D., Anne E. Egger, Ph.D.

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Did you know that when Europeans first saw chimpanzees, they thought the animals were hairy, adult humans with stunted growth? A study of chimpanzees paved the way for comparison to be recognized as an important research method. Later, Charles Darwin and others used this comparative research method in the development of the theory of evolution.

Comparison is used to determine and quantify relationships between two or more variables by observing different groups that either by choice or circumstance are exposed to different treatments.

Comparison includes both retrospective studies that look at events that have already occurred, and prospective studies, that examine variables from the present forward.

Comparative research is similar to experimentation in that it involves comparing a treatment group to a control, but it differs in that the treatment is observed rather than being consciously imposed due to ethical concerns, or because it is not possible, such as in a retrospective study.

Anyone who has stared at a chimpanzee in a zoo (Figure 1) has probably wondered about the animal's similarity to humans. Chimps make facial expressions that resemble humans, use their hands in much the same way we do, are adept at using different objects as tools, and even laugh when they are tickled. It may not be surprising to learn then that when the first captured chimpanzees were brought to Europe in the 17 th century, people were confused, labeling the animals "pygmies" and speculating that they were stunted versions of "full-grown" humans. A London physician named Edward Tyson obtained a "pygmie" that had died of an infection shortly after arriving in London, and began a systematic study of the animal that cataloged the differences between chimpanzees and humans, thus helping to establish comparative research as a scientific method .

Figure 1: A chimpanzee

• A brief history of comparative methods

In 1698, Tyson, a member of the Royal Society of London, began a detailed dissection of the "pygmie" he had obtained and published his findings in the 1699 work: Orang-Outang, sive Homo Sylvestris: or, the Anatomy of a Pygmie Compared with that of a Monkey, an Ape, and a Man . The title of the work further reflects the misconception that existed at the time – Tyson did not use the term Orang-Outang in its modern sense to refer to the orangutan; he used it in its literal translation from the Malay language as "man of the woods," as that is how the chimps were viewed.

Tyson took great care in his dissection. He precisely measured and compared a number of anatomical variables such as brain size of the "pygmie," ape, and human. He recorded his measurements of the "pygmie," even down to the direction in which the animal's hair grew: "The tendency of the Hair of all of the Body was downwards; but only from the Wrists to the Elbows 'twas upwards" (Russell, 1967). Aided by William Cowper, Tyson made drawings of various anatomical structures, taking great care to accurately depict the dimensions of these structures so that they could be compared to those in humans (Figure 2). His systematic comparative study of the dimensions of anatomical structures in the chimp, ape, and human led him to state:

in the Organization of abundance of its Parts, it more approached to the Structure of the same in Men: But where it differs from a Man, there it resembles plainly the Common Ape, more than any other Animal. (Russell, 1967)

Tyson's comparative studies proved exceptionally accurate and his research was used by others, including Thomas Henry Huxley in Evidence as to Man's Place in Nature (1863) and Charles Darwin in The Descent of Man (1871).

Figure 2: Edward Tyson's drawing of the external appearance of a "pygmie" (left) and the animal's skeleton (right) from The Anatomy of a Pygmie Compared with that of a Monkey, an Ape, and a Man from the second edition, London, printed for T. Osborne, 1751.

Tyson's methodical and scientific approach to anatomical dissection contributed to the development of evolutionary theory and helped establish the field of comparative anatomy. Further, Tyson's work helps to highlight the importance of comparison as a scientific research method .

• Comparison as a scientific research method

Comparative research represents one approach in the spectrum of scientific research methods and in some ways is a hybrid of other methods, drawing on aspects of both experimental science (see our Experimentation in Science module) and descriptive research (see our Description in Science module). Similar to experimentation, comparison seeks to decipher the relationship between two or more variables by documenting observed differences and similarities between two or more subjects or groups. In contrast to experimentation, the comparative researcher does not subject one of those groups to a treatment , but rather observes a group that either by choice or circumstance has been subject to a treatment. Thus comparison involves observation in a more "natural" setting, not subject to experimental confines, and in this way evokes similarities with description.

Importantly, the simple comparison of two variables or objects is not comparative research . Tyson's work would not have been considered scientific research if he had simply noted that "pygmies" looked like humans without measuring bone lengths and hair growth patterns. Instead, comparative research involves the systematic cataloging of the nature and/or behavior of two or more variables, and the quantification of the relationship between them.

Figure 3: Skeleton of the juvenile chimpanzee dissected by Edward Tyson, currently displayed at the Natural History Museum, London.

While the choice of which research method to use is a personal decision based in part on the training of the researchers conducting the study, there are a number of scenarios in which comparative research would likely be the primary choice.

• The first scenario is one in which the scientist is not trying to measure a response to change, but rather he or she may be trying to understand the similarities and differences between two subjects . For example, Tyson was not observing a change in his "pygmie" in response to an experimental treatment . Instead, his research was a comparison of the unknown "pygmie" to humans and apes in order to determine the relationship between them.
• A second scenario in which comparative studies are common is when the physical scale or timeline of a question may prevent experimentation. For example, in the field of paleoclimatology, researchers have compared cores taken from sediments deposited millions of years ago in the world's oceans to see if the sedimentary composition is similar across all oceans or differs according to geographic location. Because the sediments in these cores were deposited millions of years ago, it would be impossible to obtain these results through the experimental method . Research designed to look at past events such as sediment cores deposited millions of years ago is referred to as retrospective research.
• A third common comparative scenario is when the ethical implications of an experimental treatment preclude an experimental design. Researchers who study the toxicity of environmental pollutants or the spread of disease in humans are precluded from purposefully exposing a group of individuals to the toxin or disease for ethical reasons. In these situations, researchers would set up a comparative study by identifying individuals who have been accidentally exposed to the pollutant or disease and comparing their symptoms to those of a control group of people who were not exposed. Research designed to look at events from the present into the future, such as a study looking at the development of symptoms in individuals exposed to a pollutant, is referred to as prospective research.

Comparative science was significantly strengthened in the late 19th and early 20th century with the introduction of modern statistical methods . These were used to quantify the association between variables (see our Statistics in Science module). Today, statistical methods are critical for quantifying the nature of relationships examined in many comparative studies. The outcome of comparative research is often presented in one of the following ways: as a probability , as a statement of statistical significance , or as a declaration of risk. For example, in 2007 Kristensen and Bjerkedal showed that there is a statistically significant relationship (at the 95% confidence level) between birth order and IQ by comparing test scores of first-born children to those of their younger siblings (Kristensen & Bjerkedal, 2007). And numerous studies have contributed to the determination that the risk of developing lung cancer is 30 times greater in smokers than in nonsmokers (NCI, 1997).

Comprehension Checkpoint

• Comparison in practice: The case of cigarettes

In 1919, Dr. George Dock, chairman of the Department of Medicine at Barnes Hospital in St. Louis, asked all of the third- and fourth-year medical students at the teaching hospital to observe an autopsy of a man with a disease so rare, he claimed, that most of the students would likely never see another case of it in their careers. With the medical students gathered around, the physicians conducting the autopsy observed that the patient's lungs were speckled with large dark masses of cells that had caused extensive damage to the lung tissue and had forced the airways to close and collapse. Dr. Alton Ochsner, one of the students who observed the autopsy, would write years later that "I did not see another case until 1936, seventeen years later, when in a period of six months, I saw nine patients with cancer of the lung. – All the afflicted patients were men who smoked heavily and had smoked since World War I" (Meyer, 1992).

Figure 4: Image from a stereoptic card showing a woman smoking a cigarette circa 1900

The American physician Dr. Isaac Adler was, in fact, the first scientist to propose a link between cigarette smoking and lung cancer in 1912, based on his observation that lung cancer patients often reported that they were smokers. Adler's observations, however, were anecdotal, and provided no scientific evidence toward demonstrating a relationship. The German epidemiologist Franz Müller is credited with the first case-control study of smoking and lung cancer in the 1930s. Müller sent a survey to the relatives of individuals who had died of cancer, and asked them about the smoking habits of the deceased. Based on the responses he received, Müller reported a higher incidence of lung cancer among heavy smokers compared to light smokers. However, the study had a number of problems. First, it relied on the memory of relatives of deceased individuals rather than first-hand observations, and second, no statistical association was made. Soon after this, the tobacco industry began to sponsor research with the biased goal of repudiating negative health claims against cigarettes (see our Scientific Institutions and Societies module for more information on sponsored research).

Beginning in the 1950s, several well-controlled comparative studies were initiated. In 1950, Ernest Wynder and Evarts Graham published a retrospective study comparing the smoking habits of 605 hospital patients with lung cancer to 780 hospital patients with other diseases (Wynder & Graham, 1950). Their study showed that 1.3% of lung cancer patients were nonsmokers while 14.6% of patients with other diseases were nonsmokers. In addition, 51.2% of lung cancer patients were "excessive" smokers while only 19.1% of other patients were excessive smokers. Both of these comparisons proved to be statistically significant differences. The statisticians who analyzed the data concluded:

when the nonsmokers and the total of the high smoking classes of patients with lung cancer are compared with patients who have other diseases, we can reject the null hypothesis that smoking has no effect on the induction of cancer of the lungs.

Wynder and Graham also suggested that there might be a lag of ten years or more between the period of smoking in an individual and the onset of clinical symptoms of cancer. This would present a major challenge to researchers since any study that investigated the relationship between smoking and lung cancer in a prospective fashion would have to last many years.

Richard Doll and Austin Hill published a similar comparative study in 1950 in which they showed that there was a statistically higher incidence of smoking among lung cancer patients compared to patients with other diseases (Doll & Hill, 1950). In their discussion, Doll and Hill raise an interesting point regarding comparative research methods by saying,

This is not necessarily to state that smoking causes carcinoma of the lung. The association would occur if carcinoma of the lung caused people to smoke or if both attributes were end-effects of a common cause.

They go on to assert that because the habit of smoking was seen to develop before the onset of lung cancer, the argument that lung cancer leads to smoking can be rejected. They therefore conclude, "that smoking is a factor, and an important factor, in the production of carcinoma of the lung."

Despite this substantial evidence , both the tobacco industry and unbiased scientists raised objections, claiming that the retrospective research on smoking was "limited, inconclusive, and controversial." The industry stated that the studies published did not demonstrate cause and effect, but rather a spurious association between two variables . Dr. Wilhelm Hueper of the National Cancer Institute, a scientist with a long history of research into occupational causes of cancers, argued that the emphasis on cigarettes as the only cause of lung cancer would compromise research support for other causes of lung cancer. Ronald Fisher , a renowned statistician, also was opposed to the conclusions of Doll and others, purportedly because they promoted a "puritanical" view of smoking.

The tobacco industry mounted an extensive campaign of misinformation, sponsoring and then citing research that showed that smoking did not cause "cardiac pain" as a distraction from the studies that were being published regarding cigarettes and lung cancer. The industry also highlighted studies that showed that individuals who quit smoking suffered from mild depression, and they pointed to the fact that even some doctors themselves smoked cigarettes as evidence that cigarettes were not harmful (Figure 5).

Figure 5: Cigarette advertisement circa 1946.

While the scientific research began to impact health officials and some legislators, the industry's ad campaign was effective. The US Federal Trade Commission banned tobacco companies from making health claims about their products in 1955. However, more significant regulation was averted. An editorial that appeared in the New York Times in 1963 summed up the national sentiment when it stated that the tobacco industry made a "valid point," and the public should refrain from making a decision regarding cigarettes until further reports were issued by the US Surgeon General.

In 1951, Doll and Hill enrolled 40,000 British physicians in a prospective comparative study to examine the association between smoking and the development of lung cancer. In contrast to the retrospective studies that followed patients with lung cancer back in time, the prospective study was designed to follow the group forward in time. In 1952, Drs. E. Cuyler Hammond and Daniel Horn enrolled 187,783 white males in the United States in a similar prospective study. And in 1959, the American Cancer Society (ACS) began the first of two large-scale prospective studies of the association between smoking and the development of lung cancer. The first ACS study, named Cancer Prevention Study I, enrolled more than 1 million individuals and tracked their health, smoking and other lifestyle habits, development of diseases, cause of death, and life expectancy for almost 13 years (Garfinkel, 1985).

All of the studies demonstrated that smokers are at a higher risk of developing and dying from lung cancer than nonsmokers. The ACS study further showed that smokers have elevated rates of other pulmonary diseases, coronary artery disease, stroke, and cardiovascular problems. The two ACS Cancer Prevention Studies would eventually show that 52% of deaths among smokers enrolled in the studies were attributed to cigarettes.

In the second half of the 20 th century, evidence from other scientific research methods would contribute multiple lines of evidence to the conclusion that cigarette smoke is a major cause of lung cancer:

Descriptive studies of the pathology of lungs of deceased smokers would demonstrate that smoking causes significant physiological damage to the lungs. Experiments that exposed mice, rats, and other laboratory animals to cigarette smoke showed that it caused cancer in these animals (see our Experimentation in Science module for more information). Physiological models would help demonstrate the mechanism by which cigarette smoke causes cancer.

As evidence linking cigarette smoke to lung cancer and other diseases accumulated, the public, the legal community, and regulators slowly responded. In 1957, the US Surgeon General first acknowledged an association between smoking and lung cancer when a report was issued stating, "It is clear that there is an increasing and consistent body of evidence that excessive cigarette smoking is one of the causative factors in lung cancer." In 1965, over objections by the tobacco industry and the American Medical Association, which had just accepted a $10 million grant from the tobacco companies, the US Congress passed the Federal Cigarette Labeling and Advertising Act, which required that cigarette packs carry the warning: "Caution: Cigarette Smoking May Be Hazardous to Your Health." In 1967, the US Surgeon General issued a second report stating that cigarette smoking is the principal cause of lung cancer in the United States. While the tobacco companies found legal means to protect themselves for decades following this, in 1996, Brown and Williamson Tobacco Company was ordered to pay $750,000 in a tobacco liability lawsuit; it became the first liability award paid to an individual by a tobacco company.

• Comparison across disciplines

Comparative studies are used in a host of scientific disciplines, from anthropology to archaeology, comparative biology, epidemiology , psychology, and even forensic science. DNA fingerprinting, a technique used to incriminate or exonerate a suspect using biological evidence , is based on comparative science. In DNA fingerprinting, segments of DNA are isolated from a suspect and from biological evidence such as blood, semen, or other tissue left at a crime scene. Up to 20 different segments of DNA are compared between that of the suspect and the DNA found at the crime scene. If all of the segments match, the investigator can calculate the statistical probability that the DNA came from the suspect as opposed to someone else. Thus DNA matches are described in terms of a "1 in 1 million" or "1 in 1 billion" chance of error.

Comparative methods are also commonly used in studies involving humans due to the ethical limits of experimental treatment . For example, in 2007, Petter Kristensen and Tor Bjerkedal published a study in which they compared the IQ of over 250,000 male Norwegians in the military (Kristensen & Bjerkedal, 2007). The researchers found a significant relationship between birth order and IQ, where the average IQ of first-born male children was approximately three points higher than the average IQ of the second-born male in the same family. The researchers further showed that this relationship was correlated with social rather than biological factors, as second-born males who grew up in families in which the first-born child died had average IQs similar to other first-born children. One might imagine a scenario in which this type of study could be carried out experimentally, for example, purposefully removing first-born male children from certain families, but the ethics of such an experiment preclude it from ever being conducted.

• Limitations of comparative methods

One of the primary limitations of comparative methods is the control of other variables that might influence a study. For example, as pointed out by Doll and Hill in 1950, the association between smoking and cancer deaths could have meant that: a) smoking caused lung cancer, b) lung cancer caused individuals to take up smoking, or c) a third unknown variable caused lung cancer AND caused individuals to smoke (Doll & Hill, 1950). As a result, comparative researchers often go to great lengths to choose two different study groups that are similar in almost all respects except for the treatment in question. In fact, many comparative studies in humans are carried out on identical twins for this exact reason. For example, in the field of tobacco research , dozens of comparative twin studies have been used to examine everything from the health effects of cigarette smoke to the genetic basis of addiction.

• Comparison in modern practice

Figure 6: The "Keeling curve," a long-term record of atmospheric CO 2 concentration measured at the Mauna Loa Observatory (Keeling et al.). Although the annual oscillations represent natural, seasonal variations, the long-term increase means that concentrations are higher than they have been in 400,000 years. Graphic courtesy of NASA's Earth Observatory.

Despite the lessons learned during the debate that ensued over the possible effects of cigarette smoke, misconceptions still surround comparative science. For example, in the late 1950s, Charles Keeling , an oceanographer at the Scripps Institute of Oceanography, began to publish data he had gathered from a long-term descriptive study of atmospheric carbon dioxide (CO 2 ) levels at the Mauna Loa observatory in Hawaii (Keeling, 1958). Keeling observed that atmospheric CO 2 levels were increasing at a rapid rate (Figure 6). He and other researchers began to suspect that rising CO 2 levels were associated with increasing global mean temperatures, and several comparative studies have since correlated rising CO 2 levels with rising global temperature (Keeling, 1970). Together with research from modeling studies (see our Modeling in Scientific Research module), this research has provided evidence for an association between global climate change and the burning of fossil fuels (which emits CO 2 ).

Yet in a move reminiscent of the fight launched by the tobacco companies, the oil and fossil fuel industry launched a major public relations campaign against climate change research . As late as 1989, scientists funded by the oil industry were producing reports that called the research on climate change "noisy junk science" (Roberts, 1989). As with the tobacco issue, challenges to early comparative studies tried to paint the method as less reliable than experimental methods. But the challenges actually strengthened the science by prompting more researchers to launch investigations, thus providing multiple lines of evidence supporting an association between atmospheric CO 2 concentrations and climate change. As a result, the culmination of multiple lines of scientific evidence prompted the Intergovernmental Panel on Climate Change organized by the United Nations to issue a report stating that "Warming of the climate system is unequivocal," and "Carbon dioxide is the most important anthropogenic greenhouse gas (IPCC, 2007)."

Comparative studies are a critical part of the spectrum of research methods currently used in science. They allow scientists to apply a treatment-control design in settings that preclude experimentation, and they can provide invaluable information about the relationships between variables . The intense scrutiny that comparison has undergone in the public arena due to cases involving cigarettes and climate change has actually strengthened the method by clarifying its role in science and emphasizing the reliability of data obtained from these studies.

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Comparative Research

Although not everyone would agree, comparing is not always bad. Comparing things can also give you a handful of benefits. For instance, there are times in our life where we feel lost. You may not be getting the job that you want or have the sexy body that you have been aiming for a long time now. Then, you happen to cross path with an old friend of yours, who happened to get the job that you always wanted. This scenario may put your self-esteem down, knowing that this friend got what you want, while you didn’t. Or you can choose to look at your friend as an example that your desire is actually attainable. Come up with a plan to achieve your  personal development goal . Perhaps, ask for tips from this person or from the people who inspire you. According to the article posted in  brit.co , licensed master social worker and therapist Kimberly Hershenson said that comparing yourself to someone successful can be an excellent self-motivation to work on your goals.

Aside from self-improvement, as a researcher, you should know that comparison is an essential method in scientific studies, such as experimental research and descriptive research . Through this method, you can uncover the relationship between two or more variables of your project in the form of comparative analysis .

What is Comparative Research?

Aiming to compare two or more variables of an experiment project, experts usually apply comparative research examples in social sciences to compare countries and cultures across a particular area or the entire world. Despite its proven effectiveness, you should keep it in mind that some states have different disciplines in sharing data. Thus, it would help if you consider the affecting factors in gathering specific information.

Quantitative and Qualitative Research Methods in Comparative Studies

In comparing variables, the statistical and mathematical data collection, and analysis that quantitative research methodology naturally uses to uncover the correlational connection of the variables, can be essential. Additionally, since quantitative research requires a specific research question, this method can help you can quickly come up with one particular comparative research question.

The goal of comparative research is drawing a solution out of the similarities and differences between the focused variables. Through non-experimental or qualitative research , you can include this type of research method in your comparative research design.

13+ Comparative Research Examples

Know more about comparative research by going over the following examples. You can download these zipped documents in PDF and MS Word formats.

1. Comparative Research Report Template

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2. Business Comparative Research Template

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3. Comparative Market Research Template

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4. Comparative Research Strategies Example

5. Comparative Research in Anthropology Example

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6. Sample Comparative Research Example

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7. Comparative Area Research Example

8. Comparative Research on Women’s Emplyment Example

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9. Basic Comparative Research Example

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10. Comparative Research in Medical Treatments Example

11. Comparative Research in Education Example

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12. Formal Comparative Research Example

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13. Comparative Research Designs Example

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14. Casual Comparative Research in DOC

Best Practices in Writing an Essay for Comparative Research in Visual Arts

If you are going to write an essay for a comparative research examples paper, this section is for you. You must know that there are inevitable mistakes that students do in essay writing . To avoid those mistakes, follow the following pointers.

1. Compare the Artworks Not the Artists

One of the mistakes that students do when writing a comparative essay is comparing the artists instead of artworks. Unless your instructor asked you to write a biographical essay, focus your writing on the works of the artists that you choose.

2. Consult to Your Instructor

There is broad coverage of information that you can find on the internet for your project. Some students, however, prefer choosing the images randomly. In doing so, you may not create a successful comparative study. Therefore, we recommend you to discuss your selections with your teacher.

3. Avoid Redundancy

It is common for the students to repeat the ideas that they have listed in the comparison part. Keep it in mind that the spaces for this activity have limitations. Thus, it is crucial to reserve each space for more thoroughly debated ideas.

4. Be Minimal

Unless instructed, it would be practical if you only include a few items(artworks). In this way, you can focus on developing well-argued information for your study.

5. Master the Assessment Method and the Goals of the Project

We get it. You are doing this project because your instructor told you so. However, you can make your study more valuable by understanding the goals of doing the project. Know how you can apply this new learning. You should also know the criteria that your teachers use to assess your output. It will give you a chance to maximize the grade that you can get from this project.

Comparing things is one way to know what to improve in various aspects. Whether you are aiming to attain a personal goal or attempting to find a solution to a certain task, you can accomplish it by knowing how to conduct a comparative study. Use this content as a tool to expand your knowledge about this research methodology .

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What is comparative analysis? A complete guide

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Reviewed by

Jean Kaluza

Comparative analysis is a valuable tool for acquiring deep insights into your organization’s processes, products, and services so you can continuously improve them. 

Similarly, if you want to streamline, price appropriately, and ultimately be a market leader, you’ll likely need to draw on comparative analyses quite often.

When faced with multiple options or solutions to a given problem, a thorough comparative analysis can help you compare and contrast your options and make a clear, informed decision.

If you want to get up to speed on conducting a comparative analysis or need a refresher, here’s your guide.

Make comparative analysis less tedious

Dovetail streamlines comparative analysis to help you uncover and share actionable insights

• What exactly is comparative analysis?

A comparative analysis is a side-by-side comparison that systematically compares two or more things to pinpoint their similarities and differences. The focus of the investigation might be conceptual—a particular problem, idea, or theory—or perhaps something more tangible, like two different data sets.

For instance, you could use comparative analysis to investigate how your product features measure up to the competition.

After a successful comparative analysis, you should be able to identify strengths and weaknesses and clearly understand which product is more effective.

You could also use comparative analysis to examine different methods of producing that product and determine which way is most efficient and profitable.

The potential applications for using comparative analysis in everyday business are almost unlimited. That said, a comparative analysis is most commonly used to examine

Emerging trends and opportunities (new technologies, marketing)

Competitor strategies

Financial health

Effects of trends on a target audience

• Why is comparative analysis so important? 

Comparative analysis can help narrow your focus so your business pursues the most meaningful opportunities rather than attempting dozens of improvements simultaneously.

A comparative approach also helps frame up data to illuminate interrelationships. For example, comparative research might reveal nuanced relationships or critical contexts behind specific processes or dependencies that wouldn’t be well-understood without the research.

For instance, if your business compares the cost of producing several existing products relative to which ones have historically sold well, that should provide helpful information once you’re ready to look at developing new products or features.

• Comparative vs. competitive analysis—what’s the difference?

Comparative analysis is generally divided into three subtypes, using quantitative or qualitative data and then extending the findings to a larger group. These include

Pattern analysis —identifying patterns or recurrences of trends and behavior across large data sets.

Data filtering —analyzing large data sets to extract an underlying subset of information. It may involve rearranging, excluding, and apportioning comparative data to fit different criteria. 

Decision tree —flowcharting to visually map and assess potential outcomes, costs, and consequences.

In contrast, competitive analysis is a type of comparative analysis in which you deeply research one or more of your industry competitors. In this case, you’re using qualitative research to explore what the competition is up to across one or more dimensions.

For example

Service delivery —metrics like the Net Promoter Scores indicate customer satisfaction levels.

Market position — the share of the market that the competition has captured.

Brand reputation —how well-known or recognized your competitors are within their target market.

• Tips for optimizing your comparative analysis

Conduct original research

Thorough, independent research is a significant asset when doing comparative analysis. It provides evidence to support your findings and may present a perspective or angle not considered previously. 

Make analysis routine

To get the maximum benefit from comparative research, make it a regular practice, and establish a cadence you can realistically stick to. Some business areas you could plan to analyze regularly include:

Profitability

Competition

Experiment with controlled and uncontrolled variables

In addition to simply comparing and contrasting, explore how different variables might affect your outcomes.

For example, a controllable variable would be offering a seasonal feature like a shopping bot to assist in holiday shopping or raising or lowering the selling price of a product.

Uncontrollable variables include weather, changing regulations, the current political climate, or global pandemics.

Put equal effort into each point of comparison

Most people enter into comparative research with a particular idea or hypothesis already in mind to validate. For instance, you might try to prove the worthwhileness of launching a new service. So, you may be disappointed if your analysis results don’t support your plan.

However, in any comparative analysis, try to maintain an unbiased approach by spending equal time debating the merits and drawbacks of any decision. Ultimately, this will be a practical, more long-term sustainable approach for your business than focusing only on the evidence that favors pursuing your argument or strategy.

Writing a comparative analysis in five steps

To put together a coherent, insightful analysis that goes beyond a list of pros and cons or similarities and differences, try organizing the information into these five components:

1. Frame of reference

Here is where you provide context. First, what driving idea or problem is your research anchored in? Then, for added substance, cite existing research or insights from a subject matter expert, such as a thought leader in marketing, startup growth, or investment

2. Grounds for comparison Why have you chosen to examine the two things you’re analyzing instead of focusing on two entirely different things? What are you hoping to accomplish?

3. Thesis What argument or choice are you advocating for? What will be the before and after effects of going with either decision? What do you anticipate happening with and without this approach?

For example, “If we release an AI feature for our shopping cart, we will have an edge over the rest of the market before the holiday season.” The finished comparative analysis will weigh all the pros and cons of choosing to build the new expensive AI feature including variables like how “intelligent” it will be, what it “pushes” customers to use, how much it takes off the plates of customer service etc.

Ultimately, you will gauge whether building an AI feature is the right plan for your e-commerce shop.

4. Organize the scheme Typically, there are two ways to organize a comparative analysis report. First, you can discuss everything about comparison point “A” and then go into everything about aspect “B.” Or, you alternate back and forth between points “A” and “B,” sometimes referred to as point-by-point analysis.

Using the AI feature as an example again, you could cover all the pros and cons of building the AI feature, then discuss the benefits and drawbacks of building and maintaining the feature. Or you could compare and contrast each aspect of the AI feature, one at a time. For example, a side-by-side comparison of the AI feature to shopping without it, then proceeding to another point of differentiation.

5. Connect the dots Tie it all together in a way that either confirms or disproves your hypothesis.

For instance, “Building the AI bot would allow our customer service team to save 12% on returns in Q3 while offering optimizations and savings in future strategies. However, it would also increase the product development budget by 43% in both Q1 and Q2. Our budget for product development won’t increase again until series 3 of funding is reached, so despite its potential, we will hold off building the bot until funding is secured and more opportunities and benefits can be proved effective.”

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Comparative effectiveness research for the clinician researcher: a framework for making a methodological design choice

Cylie m. williams.

1 Peninsula Health, Community Health, PO Box 52, Frankston, Melbourne, Victoria 3199 Australia

2 Monash University, School of Physiotherapy, Melbourne, Australia

3 Monash Health, Allied Health Research Unit, Melbourne, Australia

Elizabeth H. Skinner

4 Western Health, Allied Health, Melbourne, Australia

Alicia M. James

Jill l. cook, steven m. mcphail.

5 Queensland University of Technology, School of Public Health and Social Work, Brisbane, Australia

Terry P. Haines

Comparative effectiveness research compares two active forms of treatment or usual care in comparison with usual care with an additional intervention element. These types of study are commonly conducted following a placebo or no active treatment trial. Research designs with a placebo or non-active treatment arm can be challenging for the clinician researcher when conducted within the healthcare environment with patients attending for treatment.

A framework for conducting comparative effectiveness research is needed, particularly for interventions for which there are no strong regulatory requirements that must be met prior to their introduction into usual care. We argue for a broader use of comparative effectiveness research to achieve translatable real-world clinical research. These types of research design also affect the rapid uptake of evidence-based clinical practice within the healthcare setting.

This framework includes questions to guide the clinician researcher into the most appropriate trial design to measure treatment effect. These questions include consideration given to current treatment provision during usual care, known treatment effectiveness, side effects of treatments, economic impact, and the setting in which the research is being undertaken.

Comparative effectiveness research compares two active forms of treatment or usual care in comparison with usual care with an additional intervention element. Comparative effectiveness research differs from study designs that have an inactive control, such as a ‘no-intervention’ or placebo group. In pharmaceutical research, trial designs in which placebo drugs are tested against the trial medication are often labeled ‘Phase III’ trials. Phase III trials aim to produce high-quality evidence of intervention efficacy and are important to identify potential side effects and benefits. Health outcome research with this study design involves the placebo being non-treatment or a ‘sham’ treatment option [ 1 ].

Traditionally, comparative effectiveness research is conducted following completion of a Phase III placebo control trial [ 2 – 4 ]. It is possible that comparative effectiveness research might not determine whether one treatment has clinical beneficence, because the comparator treatment might be harmful, irrelevant, or ineffective. This is unless the comparator treatment has already demonstrated superiority to a placebo [ 2 ]. Moreover, comparing an active treatment to an inactive control will be more likely to produce larger effect sizes than a comparison of two active treatments [ 5 ], requiring smaller sample sizes and lower costs to establish or refute the effectiveness of a treatment. Historically, then, treatments only become candidates for comparative effectiveness research to establish superiority, after a treatment has demonstrated efficacy against an inactive control.

Frequently, the provision of health interventions precedes development of the evidence base directly supporting their use [ 6 ]. Some service-provision contexts are highly regulated and high standards of evidence are required before an intervention can be provided (such as pharmacological interventions and device use). However, this is not universally the case for all services that may be provided in healthcare interventions. Despite this, there may be expectation from the individual patient and the public that individuals who present to a health service will receive some form of care deemed appropriate by treating clinicians, even in the absence of research-based evidence supporting this. This expectation may be amplified in publicly subsidized health services (as is largely the case in Canada, the UK, Australia, and many other developed nations) [ 7 – 9 ]. If a treatment is already widely employed by health professionals and is accepted by patients as a component of usual care, then it is important to consider the ethics and practicality of attempting a placebo or no-intervention control trial in this context. In this context, comparative effectiveness research could provide valuable insights to treatment effectiveness, disease pathophysiology, and economic efficiency in service delivery, with greater research feasibility than the traditional paradigm just described. Further, some authors have argued that studies with inactive control groups are used when comparative effectiveness research designs are more appropriate [ 10 ]. We propose and justify a framework for conducting research that argues for the broader use of comparative effectiveness research to achieve more feasible and translatable real-world clinical research.

This debate is important for the research community; particularly those engaged in the planning and execution of research in clinical practice settings, particularly in the provision of non-pharmacological, non-device type interventions. The ethical, preferential, and pragmatic implications from active versus inactive comparator selection in clinical trials not only influence the range of theoretical conclusions that could be drawn from a study, but also the lived experiences of patients and their treating clinical teams. The comparator selection will also have important implications for policy and practice when considering potential translation into clinical settings. It is these implications that affect the clinical researcher’s methodological design choice and justification.

The decision-making framework takes the form of a decision tree (Fig.  1 ) to determine when a comparative effectiveness study can be justified and is particularly relevant to the provision of services that do not have a tight regulatory framework governing when an intervention can be used as part of usual care. This framework is headed by Level 1 questions (demarcated by a question within an oval), which feed into decision nodes (demarcated by rectangles), which end in decision points (demarcated by diamonds). Each question is discussed with clinical examples to illustrate relevant points.

Comparative effectiveness research decision-making framework. Treatment A represents any treatment for a particular condition, which may or may not be a component of usual care to manage that condition. Treatment B is used to represent our treatment of interest. Where the response is unknown, the user should choose the NO response

Treatment A is any treatment for a particular condition that may or may not be a component of usual care to manage that condition. Treatment B is our treatment of interest. The framework results in three possible recommendations: that either (i) a study design comparing Treatment B with no active intervention could be used, or (ii) a study design comparing Treatment A, Treatment B and no active intervention should be used, or (iii) a comparative effectiveness study (Treatment A versus Treatment B) should be used.

Level 1 questions

Is the condition of interest being managed by any treatment as part of usual care either locally or internationally.

Researchers first need to identify what treatments are being offered as usual care to their target patient population to consider whether to perform a comparative effectiveness research (Treatment A versus B) or use a design comparing Treatment B with an inactive control. Usual care has been shown to vary across healthcare settings for many interventions [ 11 , 12 ]; thus, researchers should understand that usual care in their context might not be usual care universally. Consequently, researchers must consider what comprises usual care both in their local context and more broadly.

If there is no usual care treatment, then it is practical to undertake a design comparing Treatment B with no active treatment (Fig.  1 , Exit 1). If there is strong evidence of treatment effectiveness, safety, and cost-effectiveness of Treatment A that is not a component of usual care locally, this treatment should be considered for inclusion in the study. This situation can occur from delayed translation of research evidence into practice, with an estimated 17 years to implement only 14 % of research in evidence-based care [ 13 ]. In this circumstance, although it may be more feasible to use a Treatment B versus no active treatment design, the value of this research will be very limited, compared with comparative effectiveness research of Treatment A versus B. If the condition is currently being treated as part of usual care, then the researcher should consider the alternate Level 1 question for progression to Level 2.

As an example, prevention of falls is a safety priority within all healthcare sectors and most healthcare services have mitigation strategies in place. Evaluation of the effectiveness of different fall-prevention strategies within the hospital setting would most commonly require a comparative design [ 14 ]. A non-active treatment in this instance would mean withdrawal of a service that might be perceived as essential, a governmental health priority, and already integrated in the healthcare system.

Is there evidence of Treatment A’s effectiveness compared with no active intervention beyond usual care?

If there is evidence of Treatment A’s effectiveness compared with a placebo or no active treatment, then we progress to Question 3. If Treatment A has limited evidence, a comparative effectiveness research design of Treatment B versus no active treatment design can be considered. By comparing Treatment A with Treatment B, researchers would generate relevant research evidence for their local healthcare setting (is Treatment B superior to usual care or Treatment A?) and other healthcare settings that use Treatment A as their usual care. This design may be particularly useful when the local population is targeted and extrapolation of research findings is less relevant.

For example, the success of chronic disease management programs (Treatment A) run in different Aboriginal communities were highly influenced by unique characteristics and local cultures and traditions [ 15 ]. Therefore, taking Treatment A to an urban setting or non-indigenous setting with those unique characteristics will render Treatment A ineffectual. The use of Treatment A may also be particularly useful in circumstances where the condition of interest has an uncertain etiology and the competing treatments under consideration address different pathophysiological pathways. However, if Treatment A has limited use beyond the research location and there are no compelling reasons to extrapolate findings more broadly applicable, then Treatment B versus no active control design may be suitable.

The key points clinical researchers should consider are:

• The commonality of the treatment within usual care
• The success of established treatments in localized or unique population groups only
• Established effectiveness of treatments compared with placebo or no active treatment

Level 2 questions

Do the benefits of treatment a exceed the side effects when compared with no active intervention beyond usual care.

Where Treatment A is known to be effective, yet produces side effects, the severity, risk of occurrence, and duration of the side effects should be considered before it is used as a comparator for Treatment B. If the risk or potential severity of Treatment A is unacceptably high or is uncertain, and there are no other potential comparative treatments available, a study design comparing Treatment B with no active intervention should be used (Fig.  1 , Exit 2). Whether Treatment A remains a component of usual care should also be considered. If the side effects of Treatment A are considered acceptable, comparative effectiveness research may still be warranted.

The clinician researcher may also be challenged when the risk of the Treatment A and risk of Treatment B are unknown or when one is marginally more risky than the other [ 16 ]. Unknown risk comparison between the two treatments when using this framework should be considered as uncertain and the design of Treatment A versus Treatment B or Treatment B versus no intervention or a three-arm trial investigating Treatment A, B and no intervention is potentially justified (Fig.  1 , Exit 3).

A good example of risk comparison is the use of exercise programs. Walking has many health benefits, particularly for older adults, and has also demonstrated benefits in reducing falls [ 17 ]. Exercise programs inclusive of walking training have been shown to prevent falls but brisk walking programs for people at high risk of falls can increase the number of falls experienced [ 18 ]. The pragmatic approach of risk and design of comparative effectiveness research could better demonstrate the effect than a placebo (no active treatment) based trial.

• Risk of treatment side effects (including death) in the design
• Acceptable levels of risk are present for all treatments

Level 3 question

Does treatment a have a sufficient overall net benefit, when all costs and consequences or benefits are considered to deem it superior to a ‘no active intervention beyond usual care’ condition.

Simply being effective and free of unacceptable side effects is insufficient to warrant Treatment A being the standard for comparison. If the cost of providing Treatment A is so high that it renders its benefits insignificant compared with its costs, or Treatment A has been shown not to be cost-effective, or the cost-effectiveness is below acceptable thresholds, it is clear that Treatment A is not a realistic comparator. Some have advocated for a cost-effectiveness (cost-utility) threshold of $50,000 per quality-adjusted life year gained as being an appropriate threshold, though there is some disagreement about this and different societies might have different capacities to afford such a threshold [ 19 ]. Based on these considerations, one should further contemplate whether Treatment A should remain a component of usual care. If no other potential comparative treatments are available, a study design comparing Treatment B with no active intervention is recommended (Fig.  1 , Exit 4).

If Treatment A does have demonstrated efficacy, safety, and cost-effectiveness compared with no active treatment, it is unethical to pursue a study design comparing Treatment B with no active intervention, where patients providing consent are being asked to forego a safe and effective treatment that they otherwise would have received. This is an unethical approach and also unfeasible, as the recruitment rates could be very poor. However, Treatment A may be reasonable to include as a comparison if it is usually purchased by the potential participant and is made available through the trial.

The methodological design of a diabetic foot wound study illustrates the importance of health economics [ 20 ]. This study compared the outcomes of Treatment A (non-surgical sharps debridement) with Treatment B (low-frequency ultrasonic debridement). Empirical evidence supports the need for wound care and non-intervention would place the patient at risk of further wound deterioration, potentially resulting in loss of limb loss or death [ 21 ]. High consumable expenses and increased short-term time demands compared with low expense and longer term decreased time demands must also be considered. The value of information should also be considered, with the existing levels of evidence weighed up against the opportunity cost of using research funds for another purpose in the context of the probability that Treatment A is cost-effective [ 22 ].

• Economic evaluation and effect on treatment
• Understanding the health economics of treatment based on effectiveness will guide clinical practice
• Not all treatment costs are known but establishing these can guide evidence-based practice or research design

Level 4 question

Is the patient (potential participant) presenting to a health service or to a university- or research-administered clinic.

If Treatment A is not a component of usual care, one of three alternatives is being considered by the researcher: (i) conducting a comparative effectiveness study of Treatment B in addition to usual care versus usual care alone, (ii) introducing Treatment A to usual care for the purpose of the trial and then comparing it with Treatment B in addition to usual care, (iii) conducting a trial of Treatment B versus no active control. If the researcher is considering option (i), usual care should itself be considered to be Treatment A, and the researcher should return to Question 2 in our framework.

There is a recent focus on the importance of health research conducted by clinicians within health service settings as distinct from health research conducted by university-based academics within university settings [ 23 , 24 ]. People who present to health services expect to receive treatment for their complaint, unlike a person responding to a research trial advertisement, where it is clearly stated that participants might not receive active treatment. It is in these circumstances that option (ii) is most appropriate.

Using research designs (option iii) comparing Treatment B with no active control within a health service setting poses challenges to clinical staff caring for patients, as they need to consider the ethics of enrolling patients into a study who might not receive an active treatment (Fig.  1 , Exit 4). This is not to imply that the use of a non-active control is unethical. Where there is no evidence of effectiveness, this should be considered within the study design and in relation to the other framework questions about the risk and use of the treatment within usual care. Clinicians will need to establish the effectiveness, safety, and cost-effectiveness of the treatments and their impact on other health services, weighed against their concern for the patient’s well-being and the possibility that no treatment will be provided [ 25 ]. This is referred to as clinical equipoise.

Patients have a right to access publicly available health interventions, regardless of the presence of a trial. Comparing Treatment B with no active control is inappropriate, owing to usual care being withheld. However, if there is insufficient evidence that usual care is effective, or sufficient evidence that adverse events are likely, the treatment is prohibitive to implement within clinical practice, or the cost of the intervention is significant, a sham or placebo-based trial should be implemented.

Comparative effectiveness research evaluating different treatment options of heel pain within a community health service [ 26 ] highlighted the importance of the research setting. Children with heel pain who attended the health service for treatment were recruited for this study. Children and parents were asked on enrollment if they would participate if there were a potential assignment to a ‘no-intervention’ group. Of the 124 participants, only 7 % ( n  = 9) agreed that they would participate if placed into a group with no treatment [ 26 ].

• The research setting can impact the design of research
• Clinical equipoise challenges clinicians during recruitment into research in the healthcare setting
• Patients enter a healthcare service for treatment; entering a clinical trial is not the presentation motive

This framework describes and examines a decision structure for comparator selection in comparative effectiveness research based on current interventions, risk, and setting. While scientific rigor is critical, researchers in clinical contexts have additional considerations related to existing practice, patient safety, and outcomes. It is proposed that when trials are conducted in healthcare settings, a comparative effectiveness research design should be the preferred methodology to placebo-based trial design, provided that evidence for treatment options, risk, and setting have all been carefully considered.

Authors’ contributions

CMW and TPH drafted the framework and manuscript. All authors critically reviewed and revised the framework and manuscript and approved the final version of the manuscript.

Competing interests

The authors declare that they have no competing interests.

Contributor Information

Cylie M. Williams, Phone: +61 3 9784 8100, Email: ua.vog.civ.nchp@smailliweilyc .

Elizabeth H. Skinner, Email: [email protected] .

Alicia M. James, Email: ua.vog.civ.nchp@semajaicila .

Jill L. Cook, Email: [email protected] .

Steven M. McPhail, Email: [email protected] .

Terry P. Haines, Email: [email protected] .

How to Do Comparative Analysis in Research ( Examples )

Comparative analysis is a method that is widely used in social science . It is a method of comparing two or more items with an idea of uncovering and discovering new ideas about them. It often compares and contrasts social structures and processes around the world to grasp general patterns. Comparative analysis tries to understand the study and explain every element of data that comparing. 

We often compare and contrast in our daily life. So it is usual to compare and contrast the culture and human society. We often heard that ‘our culture is quite good than theirs’ or ‘their lifestyle is better than us’. In social science, the social scientist compares primitive, barbarian, civilized, and modern societies. They use this to understand and discover the evolutionary changes that happen to society and its people.  It is not only used to understand the evolutionary processes but also to identify the differences, changes, and connections between societies.

Most social scientists are involved in comparative analysis. Macfarlane has thought that “On account of history, the examinations are typically on schedule, in that of other sociologies, transcendently in space. The historian always takes their society and compares it with the past society, and analyzes how far they differ from each other.

The comparative method of social research is a product of 19 th -century sociology and social anthropology. Sociologists like Emile Durkheim, Herbert Spencer Max Weber used comparative analysis in their works. For example, Max Weber compares the protestant of Europe with Catholics and also compared it with other religions like Islam, Hinduism, and Confucianism.

To do a systematic comparison we need to follow different elements of the method.

1. Methods of comparison The comparison method

In social science, we can do comparisons in different ways. It is merely different based on the topic, the field of study. Like Emile Durkheim compare societies as organic solidarity and mechanical solidarity. The famous sociologist Emile Durkheim provides us with three different approaches to the comparative method. Which are;

• The first approach is to identify and select one particular society in a fixed period. And by doing that, we can identify and determine the relationship, connections and differences exist in that particular society alone. We can find their religious practices, traditions, law, norms etc.
•  The second approach is to consider and draw various societies which have common or similar characteristics that may vary in some ways. It may be we can select societies at a specific period, or we can select societies in the different periods which have common characteristics but vary in some ways. For example, we can take European and American societies (which are universally similar characteristics) in the 20 th century. And we can compare and contrast their society in terms of law, custom, tradition, etc. 
• The third approach he envisaged is to take different societies of different times that may share some similar characteristics or maybe show revolutionary changes. For example, we can compare modern and primitive societies which show us revolutionary social changes.

2 . The unit of comparison

We cannot compare every aspect of society. As we know there are so many things that we cannot compare. The very success of the compare method is the unit or the element that we select to compare. We are only able to compare things that have some attributes in common. For example, we can compare the existing family system in America with the existing family system in Europe. But we are not able to compare the food habits in china with the divorce rate in America. It is not possible. So, the next thing you to remember is to consider the unit of comparison. You have to select it with utmost care.

3. The motive of comparison

As another method of study, a comparative analysis is one among them for the social scientist. The researcher or the person who does the comparative method must know for what grounds they taking the comparative method. They have to consider the strength, limitations, weaknesses, etc. He must have to know how to do the analysis.

Steps of the comparative method

1. Setting up of a unit of comparison

As mentioned earlier, the first step is to consider and determine the unit of comparison for your study. You must consider all the dimensions of your unit. This is where you put the two things you need to compare and to properly analyze and compare it. It is not an easy step, we have to systematically and scientifically do this with proper methods and techniques. You have to build your objectives, variables and make some assumptions or ask yourself about what you need to study or make a hypothesis for your analysis.

The best casings of reference are built from explicit sources instead of your musings or perceptions. To do that you can select some attributes in the society like marriage, law, customs, norms, etc. by doing this you can easily compare and contrast the two societies that you selected for your study. You can set some questions like, is the marriage practices of Catholics are different from Protestants? Did men and women get an equal voice in their mate choice? You can set as many questions that you wanted. Because that will explore the truth about that particular topic. A comparative analysis must have these attributes to study. A social scientist who wishes to compare must develop those research questions that pop up in your mind. A study without those is not going to be a fruitful one.

2. Grounds of comparison

The grounds of comparison should be understandable for the reader. You must acknowledge why you selected these units for your comparison. For example, it is quite natural that a person who asks why you choose this what about another one? What is the reason behind choosing this particular society? If a social scientist chooses primitive Asian society and primitive Australian society for comparison, he must acknowledge the grounds of comparison to the readers. The comparison of your work must be self-explanatory without any complications.

If you choose two particular societies for your comparative analysis you must convey to the reader what are you intended to choose this and the reason for choosing that society in your analysis.

3 . Report or thesis

The main element of the comparative analysis is the thesis or the report. The report is the most important one that it must contain all your frame of reference. It must include all your research questions, objectives of your topic, the characteristics of your two units of comparison, variables in your study, and last but not least the finding and conclusion must be written down. The findings must be self-explanatory because the reader must understand to what extent did they connect and what are their differences. For example, in Emile Durkheim’s Theory of Division of Labour, he classified organic solidarity and Mechanical solidarity . In which he means primitive society as Mechanical solidarity and modern society as Organic Solidarity. Like that you have to mention what are your findings in the thesis.

4. Relationship and linking one to another

Your paper must link each point in the argument. Without that the reader does not understand the logical and rational advance in your analysis. In a comparative analysis, you need to compare the ‘x’ and ‘y’ in your paper. (x and y mean the two-unit or things in your comparison). To do that you can use likewise, similarly, on the contrary, etc. For example, if we do a comparison between primitive society and modern society we can say that; ‘in the primitive society the division of labour is based on gender and age on the contrary (or the other hand), in modern society, the division of labour is based on skill and knowledge of a person.

Demerits of comparison

Comparative analysis is not always successful. It has some limitations. The broad utilization of comparative analysis can undoubtedly cause the feeling that this technique is a solidly settled, smooth, and unproblematic method of investigation, which because of its undeniable intelligent status can produce dependable information once some specialized preconditions are met acceptably.

Perhaps the most fundamental issue here respects the independence of the unit picked for comparison. As different types of substances are gotten to be analyzed, there is frequently a fundamental and implicit supposition about their independence and a quiet propensity to disregard the mutual influences and common impacts among the units.

One more basic issue with broad ramifications concerns the decision of the units being analyzed. The primary concern is that a long way from being a guiltless as well as basic assignment, the decision of comparison units is a basic and precarious issue. The issue with this sort of comparison is that in such investigations the depictions of the cases picked for examination with the principle one will in general turn out to be unreasonably streamlined, shallow, and stylised with contorted contentions and ends as entailment.

However, a comparative analysis is as yet a strategy with exceptional benefits, essentially due to its capacity to cause us to perceive the restriction of our psyche and check against the weaknesses and hurtful results of localism and provincialism. We may anyway have something to gain from history specialists’ faltering in utilizing comparison and from their regard for the uniqueness of settings and accounts of people groups. All of the above, by doing the comparison we discover the truths the underlying and undiscovered connection, differences that exist in society.

Also Read: How to write a Sociology Analysis? Explained with Examples

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Causal Comparative Research: Methods And Examples

Ritu was in charge of marketing a new protein drink about to be launched. The client wanted a causal-comparative study…

Ritu was in charge of marketing a new protein drink about to be launched. The client wanted a causal-comparative study highlighting the drink’s benefits. They demanded that comparative analysis be made the main campaign design strategy. After carefully analyzing the project requirements, Ritu decided to follow a causal-comparative research design. She realized that causal-comparative research emphasizing physical development in different groups of people would lay a good foundation to establish the product.

What Is Causal Comparative Research?

Examples of causal comparative research variables.

Causal-comparative research is a method used to identify the cause–effect relationship between a dependent and independent variable. This relationship is usually a suggested relationship because we can’t control an independent variable completely. Unlike correlation research, this doesn’t rely on relationships. In a causal-comparative research design, the researcher compares two groups to find out whether the independent variable affected the outcome or the dependent variable.

A causal-comparative method determines whether one variable has a direct influence on the other and why. It identifies the causes of certain occurrences (or non-occurrences). It makes a study descriptive rather than experimental by scrutinizing the relationships among different variables in which the independent variable has already occurred. Variables can’t be manipulated sometimes, but a link between dependent and independent variables is established and the implications of possible causes are used to draw conclusions.

In a causal-comparative design, researchers study cause and effect in retrospect and determine consequences or causes of differences already existing among or between groups of people.

Let’s look at some characteristics of causal-comparative research:

• This method tries to identify cause and effect relationships.
• Two or more groups are included as variables.
• Individuals aren’t selected randomly.
• Independent variables can’t be manipulated.
• It helps save time and money.

The main purpose of a causal-comparative study is to explore effects, consequences and causes. There are two types of causal-comparative research design. They are:

Retrospective Causal Comparative Research

For this type of research, a researcher has to investigate a particular question after the effects have occurred. They attempt to determine whether or not a variable influences another variable.

Prospective Causal Comparative Research

The researcher initiates a study, beginning with the causes and determined to analyze the effects of a given condition. This is not as common as retrospective causal-comparative research.

Usually, it’s easier to compare a variable with the known than the unknown.

Researchers use causal-comparative research to achieve research goals by comparing two variables that represent two groups. This data can include differences in opportunities, privileges exclusive to certain groups or developments with respect to gender, race, nationality or ability.

For example, to find out the difference in wages between men and women, researchers have to make a comparative study of wages earned by both genders across various professions, hierarchies and locations. None of the variables can be influenced and cause-effect relationship has to be established with a persuasive logical argument. Some common variables investigated in this type of research are:

• Achievement and other ability variables
• Family-related variables
• Organismic variables such as age, sex and ethnicity
• Variables related to schools
• Personality variables

While raw test scores, assessments and other measures (such as grade point averages) are used as data in this research, sources, standardized tests, structured interviews and surveys are popular research tools.

However, there are drawbacks of causal-comparative research too, such as its inability to manipulate or control an independent variable and the lack of randomization. Subject-selection bias always remains a possibility and poses a threat to the internal validity of a study. Researchers can control it with statistical matching or by creating identical subgroups. Executives have to look out for loss of subjects, location influences, poor attitude of subjects and testing threats to produce a valid research study.

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An Effective Guide to Comparative Research Questions

Table of Contents

Comparative research questions are a type of quantitative research question. It aims to gather information on the differences between two or more research objects based on different variables. 

These kinds of questions assist the researcher in identifying distinctive characteristics that distinguish one research subject from another.

A systematic investigation is built around research questions. Therefore, asking the right quantitative questions is key to gathering relevant and valuable information that will positively impact your work.

This article discusses the types of quantitative research questions with a particular focus on comparative questions.

What Are Quantitative Research Questions?

Quantitative research questions are unbiased queries that offer thorough information regarding a study topic . You can statistically analyze numerical data yielded from quantitative research questions.

This type of research question aids in understanding the research issue by examining trends and patterns. The data collected can be generalized to the overall population and help make informed decisions. 

Types of Quantitative Research Questions

Quantitative research questions can be divided into three types which are explained below:

Descriptive Research Questions

Researchers use descriptive research questions to collect numerical data about the traits and characteristics of study subjects. These questions mainly look for responses that bring into light the characteristic pattern of the existing research subjects.

However, note that the descriptive questions are not concerned with the causes of the observed traits and features. Instead, they focus on the “what,” i.e., explaining the topic of the research without taking into account its reasons.

Examples of Descriptive research questions:

• How often do you use our keto diet app?
• What price range are you ready to accept for this product?

Comparative Research Questions

Comparative research questions seek to identify differences between two or more distinct groups based on one or more dependent variables. These research questions aim to identify features that differ one research subject from another while emphasizing their apparent similarities.

In market research surveys, asking comparative questions can reveal how your product or service compares to its competitors. It can also help you determine your product’s benefits and drawbacks to gain a competitive edge.

The steps in formulating comparative questions are as follows:

• Choose the right starting phrase
• Specify the dependent variable
• Choose the groups that interest you
• Identify the relevant adjoining text
• Compose the comparative research question

Relationship-Based Research Questions

A relationship-based research question refers to the nature of the association between research subjects of the same category. These kinds of research question assist you in learning more about the type of relationship between two study variables.

Because they aim to distinctly define the connection between two variables, relationship-based research questions are also known as correlational research questions.

Examples of Comparative Research Questions

• What is the difference between men’s and women’s daily caloric intake in London?
• What is the difference in the shopping attitude of millennial adults and those born in 1980?
• What is the difference in time spent on video games between people of the age group 15-17 and 18-21?
• What is the difference in political views of Mexicans and Americans in the US?
• What are the differences between Snapchat usage of American male and female university students?
• What is the difference in views towards the security of online banking between the youth and the seniors?
• What is the difference in attitude between Gen-Z and Millennial toward rock music?
• What are the differences between online and offline classes?
• What are the differences between on-site and remote work?
• What is the difference between weekly Facebook photo uploads between American male and female college students?
• What are the differences between an Android and an Apple phone?

Comparative research questions are a great way to identify the difference between two study subjects of the same group.

Asking the right questions will help you gain effective and insightful data to conduct your research better . This article discusses the various aspects of quantitative research questions and their types to help you make data-driven and informed decisions when needed.

Abir Ghenaiet

Abir is a data analyst and researcher. Among her interests are artificial intelligence, machine learning, and natural language processing. As a humanitarian and educator, she actively supports women in tech and promotes diversity.

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The Impact of Eco-Labeling on Customers’ Green Purchase Intention: A Comparative Study Between Cargills Food City and Lanka Sathosa Supermarkets in Polonnaruwa District

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(Assistant Lecturer Department of Management, Faculty of Commerce and Management, Eastern University, Sri Lanka.)

(Senior Lecturer Department of Management, Faculty of Commerce and Management, Eastern University, Sri Lanka.)

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