An In-Depth Look at Study Designs and Methodologies

This appendix provides an in-depth look at study designs and methodologies. It first reviews selected designs (regression discontinuity designs, interrupted time series analysis, observational studies, pre-/posttest designs, and economic cost analysis) commonly used as alternatives to randomized experiments. It concludes with guidance on how to use theory, professional experience, and local wisdom to adapt the evidence gathered to local settings, populations, and times.


Reichardt (2006) presents a typology that encompasses the full range of randomized and strong quasi-experimental nonrandomized designs (see Table E-1). This typology is useful because it can substantially broaden the range of design options that can be considered by researchers. Reichardt considers all possible designs that can be created

TABLE E-1 A Typology of Research Designs

Prominent Size-of-Effect Factor

Assignment to Treatment



Explicit Quantitative Ordering

No Explicit Quantitative Ordering


Randomized recipient design

Regression discontinuity design

Nonequivalent recipients design


Randomized time design

Interrupted time series design

Nonequivalent times design


Randomized setting design

Discontinuity across settings design

Nonequivalent settings design

Outcome variables

Randomized outcome variable design

Discontinuity across outcome variables design

Nonequivalent outcome variables design

SOURCE: Reichardt, 2006.

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E An In-Depth Look at Study Designs and Methodologies T his appendix provides an in-depth look at study designs and methodologies. It first reviews selected designs (regression discontinuity designs, interrupted time series analysis, observational studies, pre-/posttest designs, and economic cost analysis) com- monly used as alternatives to randomized experiments. It concludes with guidance on how to use theory, professional experience, and local wisdom to adapt the evidence gathered to local settings, populations, and times. COMMON RESEARCH DESIGNS Reichardt (2006) presents a typology that encompasses the full range of randomized and strong quasi-experimental nonrandomized designs (see Table E-1). This typology is useful because it can substantially broaden the range of design options that can be considered by researchers. Reichardt considers all possible designs that can be created TABLE E-1 A Typology of Research Designs Prominent Assignment to Treatment Size-of- Nonrandom Effect Factor Random Explicit Quantitative Ordering No Explicit Quantitative Ordering Recipients Randomized recipient design Regression discontinuity design Nonequivalent recipients design Times Randomized time design Interrupted time series design Nonequivalent times design Settings Randomized setting design Discontinuity across settings design Nonequivalent settings design Outcome Randomized outcome Discontinuity across outcome Nonequivalent outcome variables variables variable design variables design design SOURCE: Reichardt, 2006. 

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based on the combination of two dimensions: assignment rule and primary dimension for assignment of units. With respect to assignment rule, units can be assigned (1) according to a ran- domized allocation scheme, (2) on the basis of a quantitative assignment rule, or (3) according to an unknown assignment rule. Randomization schemes in which each unit has an equal probability of being in a given treatment condition are familiar. A quantitative assignment rule means that there is a fixed rule for assigning units to the intervention on the basis of a quantitative measure, typically of need, merit, or risk. For example, organ transplants are allocated on the basis of a weighted combina- tion of patient waiting time and the quality of the match of the available organ to the patient. Finally, unknown assignment rules commonly apply when units self-select into treatments or researchers give different treatments to preexisting groups (e.g., two communities, two school systems). Unknown assignment rules are presumed to be nonrandom. With respect to units, participants (people or small clusters of people), times, settings, or outcome measures may serve as the units of analysis. Research in public health and medicine commonly assigns treatments to individual (or small groups of) participants. But other units of assignment are possible and should be entertained in some research contexts. Time can be the unit of assignment, as, for example, in some drug research in which short-acting drugs are introduced and withdrawn, or behavior modification interventions are introduced and withdrawn to study their effects on the behavior of single patients. Settings can be the unit of assignment, as when different community health settings are given different treatments, or different intersections are given different treatments (e.g., photo radar monitoring of speeding in a traffic safety study). Finally, even outcome measures can be assigned to different conditions. In a study of the effectiveness of the Sesame Street program, for example, different sets of commonly used letters (e.g., [a, o, p, s] versus [e, i, r, t]) could be selected for inclu- sion in the program. The knowledge of the specific letters chosen for inclusion in the program could be compared with the knowledge of the control letters to assess the program’s effectiveness. Once again, each of these types of units could potentially be assigned to treatment conditions using any of the three assignment rules. Reichardt provides a useful heuristic framework for expanding thinking about strong alternative research designs. When individuals are not the unit of analysis, however, complications may arise in the statistical analysis. These complications are addressable. In this section, some commonly utilized quasi-experimental designs from Reichardt’s framework are described. First, two designs involving nonrandom, quan- titative assignment rules—the regression discontinuity design and the interrupted time series design—are discussed. Next, the observational study (also known as the nonequivalent control group design or nonequivalent recipients design), in which the basis for assignment is unknown, is considered. Finally, the pre-experimental pre–post design, commonly utilized by decision makers, is discussed. For each design, Bridging the Evidence Gap in Obesity Prevention 

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Campbell’s and Rubin’s perspectives (detailed in Chapter 8) are brought into the dis- cussion as the basis for suggestions for enhancements that may lead to stronger causal inferences. Regression Discontinuity (RD) Design Often society prescribes that treatments be given to those with the greatest need, risk, or merit. A quantitative measure is assessed at baseline (or a composite measure is created from a set of baseline measures), and participants scoring above (or below) a threshold score are given the treatment. To cite three examples from the educational arena, access to free lunches is often given to children whose parents have an income below a specified threshold (e.g., the poverty line), whereas children above the poverty line do not receive free lunches. The recognition of dean’s list is awarded only to stu- dents who achieve a specified grade point average (e.g., 3.5 or greater). And children who reach their sixth birthday by December 31 are enrolled in first grade the follow- ing August, whereas younger children are not. Given assessment of the outcome fol- lowing the intervention, comparison of the outcomes at the threshold for the interven- tion and in control groups permits strong causal inferences to be drawn. To understand the RD design, consider the example of evaluating the effective- ness of school lunch programs on health, which is illustrated in Figure E-1. In the figure, all children with a family income of less than $20,000 qualify for the program, whereas children whose families exceed this threshold do not. The outcome measure (here a measure of health problems, such as number of school absences or school nurse visits) is collected for each child. In modeling the relationship between the known quantitative assignment variable (family income) and the outcome, the treat- ment effect will be represented by the difference in the levels of the regression lines at the cutpoint. In the basic RD design, treatment assignment is determined entirely by the assignment variable. Proper modeling of the relationship between the assignment variable and the outcome permits a strong inference of a treatment effect if there is a discontinuity at the cutpoint. Ludwig and Miller (2007) used this design to study some of the educational and health effects of the implementation of the original Head Start program in 1965. When the program was launched, counties were invited to submit applications for Head Start funding. In a special program, the 300 poorest counties in the United States (poverty rates exceeding a threshold of 59.2 percent) received technical assis- tance in writing the Head Start grant proposal. Because of the technical assistance intervention, a very high proportion (80 percent) of the poorest counties received funding, approximately twice the rate of slightly better-off counties (49.2 percent to 59.2 percent poverty rates) that did not receive this assistance. The original Head Start program included not only its well-known educational program, but also basic health services to children (e.g., nutrition supplements and education, immunization, screen- ing). In addition to positive effects on educational achievement, Ludwig and Miller  Appendix E

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0 20,000 40,000 60,000 80,000 100,000 FIGURE E-1 Illustration of the regression discontinuity design using the example of an evaluation of the effect of school lunch Figure E-1.eps programs on children’s health. NOTE: All children whose family income was below the threshold, fixed ima (dotted line), received the treatment program low-res bitmap, here $20,000ge (school lunch program); all children whose family income was above the threshold did not receive the program. The difference between the regression lines for the program and no-program groups at the threshold represents the treatment effect. SOURCE: West et al., 2008. Reprinted with permission. West et al., Alternatives to the randomized controlled trial, American Journal of Public Health, 98(8):1364, Copyright © 2008 by the American Public Health Association. found results demonstrating lower mortality rates in children aged 5 to 9 from dis- eases addressed by the program (e.g., measles, anemia, diabetes). The RD design overcomes several of the objections to the randomized controlled trial (RCT) discussed in this report. When an existing program uses quantitative assignment rules, the RD design permits strong evaluation of the program without the need to create a pool of participants willing to be randomized. Sometimes outcome data may be collected routinely from large samples of individuals in the program. As illustrated by the Ludwig and Miller study, the design can be used when individual participants, neighborhoods, cities, or counties are the unit of assignment. When new programs are implemented, assignment on the basis of need or risk may be more acceptable to communities that may be resistant to RCTs. The use of a clinically meaningful quantitative assignment variable (e.g., risk level) may help overcome ethi- cal or political objections when a promising potential treatment is being evaluated. Given that the design can often be implemented with the full population of interest—a state, community, school, or hospital—it provides direct evidence of population-level effects. Bridging the Evidence Gap in Obesity Prevention 280

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The RD design is viewed as one of the strongest alternatives to the RCT from both Campbell’s (Cook, 2008; Shadish et al., 2002; Trochim, 1984) and Rubin’s (Imbens and Lemiuex, 2008; Rubin, 1977) perspectives. However, it introduces two new challenges to causal inference that do not characterize the RCT. First, it is assumed that the functional form of the relationship between the quantitative assign- ment variable and the outcome is properly modeled. Early work on the RD design in the behavioral sciences typically assumed that a regression equation representing a linear effect of the assignment score on the outcome plus a treatment effect estimated at the cutoff would be sufficient to characterize the relationship. More recent work in econometrics has emphasized the use of alternative methods to characterize the relationship between the assignment variable and the outcome separately above and below the threshold level. For example, with large sample sizes, nonparametric regres- sion models can be fit separately above and below the threshold to minimize any pos- sibility that the functional form of the relationship is not properly specified. Second, in some RD designs, the quantitative assignment variable does not fully determine treat- ment assignment. Econometricians make a distinction between “sharp” RD designs, in which the quantitative assignment variable fully determines treatment assignment, and “fuzzy” RD designs, in which a more complex treatment selection model determines assignment. These latter designs introduce considerably more complexity, but new statistical modeling techniques based on the potential outcomes perspective (see Hahn et al., 2001) minimize any bias in the estimate of treatment effects. From Campbell’s perspective, several design elements can potentially be used to strengthen the basic design. Replication of the original study using a different thresh- old can help rule out the possibility that some form of nonlinear growth accounts for the results. Masking (blinding) the threshold score from participants, test scor- ers, and treatment providers, when possible, can minimize the possibility that factors other than the quantitative assignment variable determine treatment. Investigating the effects of the intervention on a nonequivalent dependent variable that is expected to be affected by many of the same factors as the primary outcome variable, but not the treatment, can strengthen the inference. In the case of fuzzy RD designs, sensitivity analyses in which different plausible assumptions are made about alternative function- al forms of the relationship and selection models can also be conducted. Interrupted Time Series (ITS) Analysis Often policy changes go into effect on a specific date. To illustrate, the Federal Communications Commission (FCC) allowed television broadcasting to be introduced for the first time in several medium-sized cities in the United States in 1951. Bans on indoor smoking have been introduced in numerous cities (and states) on specific dates. If outcome data can be collected or archival data are available at regular fixed intervals (e.g., weekly, monthly), the ITS provides a strong design for causal inference. The logic of the ITS closely parallels that of the RD design except that the threshold  Appendix E

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on the time rather than the baseline covariate is the basis for treatment assignment (Reichardt, 2006). Khuder and colleagues (2007) present a nice illustration of an ITS. An Ohio city instituted a ban on smoking in indoor workplaces and public places in March 2002. All cases of angina, heart failure, atherosclerosis, and acute myocardial infarction in city hospitals were identified from hospital discharge data. Following the introduction of the smoking ban, a significant reduction of heart disease−related hospital admis- sions was seen. From a design standpoint, causal inferences from the simple ITS perspective need to be tempered because the basic design fails to address three major threats to the certainty of the causal relationship between an intervention and the observed out- comes (internal validity) (Shadish et al., 2002; West et al., 2000). First, some other confounding event (e.g., introduction of a new heart medication) may occur at about the same time as the introduction of the intervention. Second, some interventions may change the population of participants in the area. For example, some cities have offered college scholarships to all students who graduate from high school. In such cases, in addition to any effect of the program on the achievement of city residents, the introduction of the program may foster immigration of highly education-oriented families to the city, changing the nature of the student population. Third, record- keeping practices may change at about the time of the intervention. For example, new criteria for the diagnosis of angina or myocardial infarction may change the number of heart disease cases even in the absence of any effect of the intervention. From a statistical standpoint, several potential problems with longitudinal data need to be addressed. Any long-term natural trends (e.g., a general decrease in heart disease cases) or cycles (e.g., more admissions during certain seasons of the year) in the data need to be modeled so their effects can be removed. In addition, time series data typically reflect serial dependence: observations closer in time tend to be more similar than observations further apart in time. These problems need to be statistically modeled to remove their effects, permitting proper estimates of the causal effect of the intervention and its standard error. Time series analysis strategies have been developed to permit researchers to address these issues (e.g., Chatfield, 2004). In addition, as in the RD design, the actual introduction of the intervention may be fuzzy. In the Khuder et al. study, for example, there was evidence that the enforcement and full implemen- tation of the smoking ban required some months after the ban was enacted. In such cases, a function describing the pattern of implementation of the intervention may need to be included in the model (e.g., Hennigan et al., 1982). In the Campbell tradition, causal inferences drawn from the basic ITS design can be greatly strengthened by the addition of design elements that address threats to validity. Khuder and colleagues included another, similar Ohio city that did not institute a smoking ban (control series), finding no parallel change in heart disease admissions after the March 2002 timepoint when the smoking ban was introduced in the treatment city. They also found that hospital admissions for diagnoses unrelated Bridging the Evidence Gap in Obesity Prevention 

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to smoking did not change in either city after March 2002 (nonequivalent dependent variable). In some time series applications, a design element known as switching rep- lications can be used, which involves locating another, similar city in which the inter- vention was introduced at a different timepoint. In their study of the introduction of television and its effects on crime rates, for example, Hennigan and colleagues (1982) located 34 medium-sized cities in which television was introduced in 1951 and 34 cit- ies matched for region and size in which television was introduced in 1954 following the lifting of a freeze on new broadcasting licenses by the FCC. They found a similar effect of the introduction of television on crime rates (e.g., an increase in larceny) beginning in 1951 in the prefreeze cities and in 1954 in the postfreeze cities. In both the Khuder et al. and Hennigan et al. studies, the addition of the design element great- ly reduced the likelihood that any threat to the level of certainty of the causal infer- ence (internal validity) could account for the results obtained. As with the RD design, moreover, the ITS design can often be implemented with the full population of interest so that it provides direct evidence of population-level effects. Observational Studies The observational study (also known as the nonequivalent control group design) is a quasi-experimental design that is commonly used in applied research on interven- tions, likely because of its ease of implementation. In this design, a baseline measure and a final outcome measure are collected on all participants. Following the baseline measurement, one group is given the treatment, while the second, comparison group does not receive the treatment. The groups may be preexisting (e.g., schools, com- munities), or unrelated participants may self-select into the treatment in some man- ner. For example, Roos and colleagues (1978) used this design to compare the health outcomes of children who received and did not receive tonsillectomies in a province of Canada. The bases on which the selection into the tonsillectomy treatment occurred were unknown and presumed to be nonrandom, possibly depending on such factors as the child’s medical history, the family, the physician, and the region. The challenge of this design is that several threats associated with possible interactions between selec- tion and other threats to level of certainty (internal validity) might be plausible. These threats must be addressed if strong causal inferences are to be drawn. To illustrate this design, consider an evaluation of a campaign to increase sales of lottery tickets (Reynolds and West, 1987). State lottery tickets are sold primarily in convenience stores and contribute to general state revenue or revenue for targeted programs (e.g., education) in several states. The stores refused randomization, ruling out an RCT. The Arizona lottery commission wished to evaluate the effectiveness of a sales campaign to increase lottery ticket sales in an 8-week-long lottery game. In the “Ask for the Sale” campaign, store clerks were instructed to ask each adult cus- tomer during checkout if he or she wished to purchase a lottery ticket. A nearby sign  Appendix E

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informed customers that if the sales clerk did not ask them, they would get a lottery ticket for free. From Campbell’s perspective, four threats to the level of certainty (internal validity) in this example observational study could interact with selection and under- mine causal inference regarding the intervention and the observed outcomes (Shadish et al., 2002): • Selection × history interaction—Some other event unrelated to the treatment could occur during the lottery game that would affect sales. Control stores could be disproportionately affected by nearby highway construction, for example, resulting in a decrease in customer traffic. • Selection × maturation interaction—Sales in treatment stores could be growing at a faster rate than sales in control stores even in the absence of the treatment. • Selection × instrumentation interaction—The nature of the measurement of lot- tery ticket sales in the treatment stores could change during the game in the treatment but not the control group. For example, stores in the treatment group could switch disproportionately from manual reporting of sales to more com- plete computer recording of sales. • Selection × statistical regression interaction—Stores having unusually low sales in the previous lottery game could self-select to be in the treatment group. Sales could return to normal levels even in the absence of the intervention. Reynolds and West (1987) matched treatment and control stores on sales in the prior game and on ZIP code (a proxy for neighborhood socioeconomic status). As shown in Figure E-2, they implemented the basic observational study design and then added several design features to address possible threats to the certainty of the causal relationship (internal validity). Panel (a) displays the results of the basic design, showing no difference in sales in the prior game (game 10, no program intervention in both stores, i.e., baseline) but greater sales in the treatment stores during the campaign (game 11) compared with matched control stores with no program intervention. Panel (b) displays the results from a set of nonequivalent dependent measures, sales catego- ries that would be expected to be affected by other general factors that affect sales but not by the intervention. The increase in sales of lottery tickets was greater than the increase for other sales categories. Panel (c) displays the results from a short time series of observations in which the sales campaign was implemented in the treatment stores in week 4 of the game. The results show that both the treatment and control stores experienced similar levels of sales each week prior to the intervention, but that the treatment stores sold far more tickets each week following the initiation of the campaign at the beginning of week 5 (i.e., “program started” in Figure E-2). Taken together, the pattern of results presented by the basic design and the additional design elements provided strong support for the effectiveness of the sales campaign. Bridging the Evidence Gap in Obesity Prevention 

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FIGURE E-2 Design elements that strengthen causal inferences in observational studies. NOTE: (a) Matching. Treatment and control stores were selected from the same chain, were in the same geographic location, and were comparable in sales during the baseline (lottery game 10). Introduction of the treatment at the beginning of lottery game 11 yielded an increase in sales only in the treatment stores. (b) Nonequivalent dependent variables. Within the treatment stores, sales of lottery tickets increased substantially following the introduction of the treatment. Sales of other major catego- ries (gasoline, cigarettes, nontaxable groceries, and taxable groceries) that would be expected to be affected by confounding factors but not the treatment did not show appreciable change. (c) Repeated pre- and posttest measurements. Treatment and control stores’ sales showed comparable trends during the 4 weeks prior to the introduction of the treatment. The level of sales in the treatment and control stores was similar prior to the introduction of the treatment, but differed substantially beginning immediately after the treatment was introduced. SOURCE: Adapted from Reynolds and West, 1987. Reynolds, K. D., and S. G. West, Evaluation Review 11:691-714, Copyright © 1987 by SAGE Publications. Reprinted by permission of SAGE Publications. 285 Appendix E

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Rubin’s (2006) perspective takes an alternative approach, attempting to create high-quality matches between treatment and control cases on all variables measured at baseline. Two recent developments in the technology of matching procedures have greatly improved the quality of matches that can be achieved. Historically, the number of variables on which high-quality matches could be achieved was limited because of the difficulty of finding cases that matched on several different variables. Rosenbaum and Rubin (1983) developed the idea of matching on the propensity score—the prob- ability that the case would be in the treatment group based on measured background variables. They proved mathematically that if close matches between cases in the treat- ment and control groups could be achieved on the propensity score, the two groups would also be closely balanced on all baseline variables from which the propensity score was constructed. Propensity scores are typically created on the basis of a logistic regression equation in which the probability of being in the treatment group based on the measured covariates is estimated (see Schafer and Kang, 2008, for a discus- sion of available techniques). The distributions of each separate baseline covariate in the treatment and control groups can be compared to ensure that close matches have been achieved. Second, new optimal matching algorithms for pairing cases in the two groups maximize the comparability of the groups’ propensity scores (Rosenbaum, 2002). The central challenge for these modern matching procedures is ensuring that all important covariates related to both the treatment group and the outcome have been included in the construction of the propensity score. Otherwise stated, have “identi- cal” units been created by the matching procedures? Wu and colleagues (2008a,b; see also West and Thoemmes, 2010) used these procedures in a study of the effect of retention in first grade on children’s subsequent math and reading achievement. Based on input from subject matter experts, they measured 72 variables at baseline believed to possibly be related to retention, achieve- ment, or both. Propensity scores were constructed using logistic regression. From 784 children who were below the median at school entrance, 97 pairs that were close- ly matched on the propensity scores were constructed using optimal matching proce- dures. Figure E-3 shows that the distribution of the retained and promoted groups on propensity scores became closely balanced following the use of the optimal matching procedures. The use of propensity scores helps rule out the possibility that preexisting differences (selection bias) between the groups could account for the results obtained. The central challenge of the propensity score procedure is ensuring that the groups have been closely balanced on all important covariates. For example, match- ing on a few demographic variables is unlikely to represent fully all of the important baseline differences between the groups (Rubin, 2006). Checks on the balance for each individual covariate can be performed, and propensity scores can be reestimated or specific controls for unbalanced covariates included in the statistical models. Finally, researchers can conduct sensitivity analyses to explore how much the results would change if important covariates were omitted from the propensity score model. Bridging the Evidence Gap in Obesity Prevention 

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Before matching Promoted (n = 604) 30 400 20 Frequency Frequency 300 200 10 100 0 0 0.05 0.15 0.25 0.35 0.45 0.55 0.65 0.75 0.85 0.95 0.05 0.15 0.25 0.35 0.45 0.55 0.65 0.75 0.85 0.95 Propensity score Propensity score After matching Promoted (n = 97) Retained (n = 97) 20 20 15 Frequency 15 Frequency 10 10 5 5 0 0 0.05 0.15 0.25 0.35 0.45 0.55 0.65 0.75 0.85 0.95 0.05 0.15 0.25 0.35 0.45 0.55 0.65 0.75 0.85 0.95 Propensity score Propensity score FIGURE E-3 The distributions of propensity score before and after matching in a study of the effects of retention in first grade on children’s subsequent math and reading achievement. NOTE: The Figurethe-y‑axis (frequency) differs between the two top panels (before matching), but is identical for the two bot‑ scale of E 3 tom panels (after matching). SD = standard deviation. SOURCE: Wu et al., 2008b. Pre-/Posttest Designs Sometimes researchers believe that designs involving a pretest (baseline), a treatment, and a posttest (outcome) measure are sufficient to evaluate the effects of interventions. Such designs are attractive because of their ease of implementation, but they are far weaker in terms of causal inference than experimental and quasi-experimental designs. Campbell and Stanley (1966) present these designs in detail, considering them in a separate, weaker class of “pre-experimental” designs. The following threats to the level of certainty (internal validity) characterize the pretest−posttest design: • History—Some other event unrelated to the treatment occurs between the pre- test and posttest that could cause the observed effect in the absence of a treat- ment effect. • Maturation—Maturational growth or decline in individuals (or secular trends in larger units) could cause the observed effect in the absence of a treatment effect. 287 Appendix E

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A second key distinction relates to a focus on the “gross” versus the “net” costs of a given behavior. The prevalence-based approach produces an estimate of gross costs—those that result from the consequences of obesity in a given year, for example. In contrast, the incidence-based approach produces an estimate of net costs, reflect- ing the trade-offs between higher average annual costs for an obese individual and the extra costs that result from a nonobese individual’s living longer. When one is compar- ing gross and net costs, a particularly controversial issue relates to what has come to be known as the “death benefit,” that is, whether the “savings” that result from lower pension and social security payments that an obese individual who dies prematurely will not collect should be included in the cost accounting. MATCHING, MAPPING, POOLING, AND PATCHING Despite best efforts to amass available evidence, decision makers grappling with an emergent problem such as obesity will face inevitable decisions that must be made and actions that must be taken in the relative absence of evidence. This section offers use- ful methods for combining evidence with theory, expert opinion, experience, and local wisdom about local traditions and probable responses to proposed actions in a pro- cess that has been described as “matching, mapping, pooling, and patching” (Green and Glasgow, 2006; Green and Kreuter, 2005, pp. 197-203). Matching Matching refers to aligning the source of evidence with the targets of an interven- tion. The evidence from different disciplines of science and research is distributed according to the level (individual, family, organization, or community) at which it was generated and matched to the level(s) of the proposed intervention and its intended impact (McLeroy et al., 1988; Richard et al., 1996; Sallis et al., 2008). Evidence from psychology and medicine generally focuses on the individual, while evidence from sociology and public health generally applies to groups, organizations, and popula- tions. The ecological thinking and recognition of social determinants of health implicit in this approach have seen a renaissance in public health in recent decades (Berkman and Kawachi, 2000; Best et al., 2003; French et al., 2001; Richard et al., 1996; Sallis et al., 2008). The usual representation of the ecological model in public health and health promotion is a set of concentric circles or ovals, as illustrated in Chapter 1 (see Figure 1-5) (e.g., Booth et al., 2001; Green and Kreuter, 2005, p. 130; IOM, 2007; National Committee on Vital and Health Statistics, 2002). For example, an ecological approach to planning a comprehensive childhood obesity control intervention would involve matching evidence of an intervention’s effectiveness with each ecological level to which the evidence might apply: Bridging the Evidence Gap in Obesity Prevention 0

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• evidence from studies of individual change in diet and physical activity, particu- larly from clinical studies and evaluations of obesity control programs directed at individuals and small groups; • evidence from studies of family, community, and cultural groups regarding group or population changes, and evaluations of change in response to mass communication or organizational or environmental changes; and • evidence from policy studies, public health evaluations, and epidemiological studies—for example, the impact of school lunch programs on food consump- tion patterns, or the impact of policies, executive decisions, and regulatory enforcement of codes for construction of sidewalks or hiking or bike paths on community physical activity patterns. The preponderance of evidence, especially that judged worthy of inclusion in systematic reviews for evidence-based practice guidelines, tends to be derived from studies of the impact of interventions on individuals. Yet there is widespread agree- ment that further progress in controlling obesity will require policy changes, orga- nizational changes, changes in the built environment, and changes in social norms, all of which require interventions and measurement of change at levels beyond the individual. An example of an ecological model that illustrates the matching process is the Multilevel Approach to Community Health (MATCH) model of B. G. Simons-Morton and colleagues (1995) (see Figure E-4). The MATCH model suggests the alignment of evidence with each of the four levels shown by the vertical arrangement of boxes in the figure. It grew out of a conceptualization of intervention research (Parcel, 1987; D. G. Simons-Morton et al., 1988a), and was applied in a series of Intervention Handbooks published by the Centers for Disease Control and Prevention (CDC), including one on promoting physical activity among adults (D. G. Simons-Morton et al., 1988b), one on a series of reviews on health-related physical fitness in child- hood (B. G. Simons-Morton et al., 1988a), and one on implementing organizational changes to promote healthful diet and physical activity in schools (B. G. Simons- Morton et al., 1988b). Other ecological models have been suggested for planning and evaluating overall programs (e.g., Green and Kreuter, 2005; Richard et al., 1996) or components of programs such as mass communications (Abroms and Maibach, 2008), and for integrating knowledge for community partnering (Best et al., 2003). The MATCH model is a first step in blending evidence from various sources for the design of a comprehensive intervention that will address the various levels at which evidence is needed and for which adaptations and innovations will be necessary when the evi- dence is lacking at specific levels.  Appendix E

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Phase 2 : Intervention Planning Phase 1: Health Goals Selection SELECT INTERVENTION IDENTIFY TARGETS SELECT INTERVENTION APPROACHES OF INTERVENTION OBJECTIVES Healthful Governments: Government and Influence Governments: Community Leader s: Policies Political process Ordinances /legislation Special action Legislator s Enforcement Social change Regulators Regulation Community development Enforcer s Resource allocation Agency administrators Program Community Facilities organization leader s Healthful Communities: Community Norm Influence Communities : Phase 3 : Shapers: Social change Facilities Development Community leader s Political action Activities Community development Residents Resources Community organizations Practices Phase 4 : Resource development Norms Implementation Education Communications Coalitions Organization Decision - Influence Organizations: Healthful Organizations: Makers : Organizational change Policies Consulting Administrators Practices Training Managers Programs Networking Internal change agents Facilities Workers/ employees Resources Union members and leader s Individuals at Risk: Influence Individuals: Healthful Individuals: Health Status : Students Education Behavior Mortalit y Training Workers Risk Factors Morbidity Residents Persuasion Wellness CONDUCT PROCESS CONDUCT IMPACT CONDUCT OUTCOME EVALUATION EVALUATION EVALUATION Phase 5 : Evaluation FIGURE E-4 The Multilevel Approach to Community Health (MATCH) model used to align the source of evidence with the tar- gets of an intervention, plan and evaluate programs, and integrate knowledgeeps Figure E-4. for community partnering. SOURCE: B. G. Simons-Morton et al., 1995. Reprinted by permission of Waveland Press, Inc. from B. G. Simons-Morton, W. H. Greene, and N. H. Gottlieb, Introduction to health education and promotion, 2nd ed. Long Grove, IL: Waveland Press, Inc., 1995, All rights reserved. Bridging the Evidence Gap in Obesity Prevention 292

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Mapping Mapping refers to tracing the causal chains or mechanisms of change inferred when evidence is matched with levels of intervention and change. The evidence will be incomplete at each ecological level with respect to the local or state circumstances in which a decision and action must be taken, but theory can (and will, formally or informally, consciously or unconsciously) be brought to bear. People naturally impose their own assumptions about causes and needed actions, and these constitute, in the crudest sense, theories of the problem and the solution. A formal process of mapping objectives, evidence, and formal theories of behavior and social change to the design of coherent, practical interventions includes guidelines for how to assess evidence and theories (Bartholomew et al., 2006). For example, Schaalma and Kok (2006) describe their development of an HIV prevention program using theory to guide their selection of determinants of behavior and the environment (e.g., knowledge, risk perceptions, attitudes, social influences, self-efficacy) relevant to the health problem (e.g., safe sex). Using this process of mapping the objectives of the intervention, existing evidence (both qualitative and quantitative), and theory, the authors were able to identify theo- retical methods of behavior change (e.g., social cognitive theory) and translate them into practical strategies (e.g., video-guided role playing). The mapping of theory helps the decision maker fill gaps in the evidence and consider how the evidence from a distant source and a particular population may or may not apply to the local setting, circumstances, and population. Too often, the published literature in a discipline will provide little if any detail about the theory on which an intervention was based, sometimes because the study was not designed to test a theory, sometimes out of reluctance or inability to be explicit about the theory, and sometimes because editors of health science journals prefer to devote space to methodological detail and data analysis rather than theory. Greenhalgh and colleagues (2007, p. 861) suggest shifting “the balance in what we define as quality from an exclusive focus on empirical method (the extent to which authors have adhered to the accepted rules of controlled trials) to one that embraces theory (the extent to which a theoretical mechanism was explicitly defined and tested).” Although theory may not be the interest of the end users of evidence, they will, as noted, have their own assumptions in the form of tacit theories. This step will ben- efit from their consultation with those who have experience with the problem and understand the scientific literature and its formally tested theories of causation and change. Pooling Much of the published evidence in obesity-related research is epidemiological or obser- vational, linking the intermediate causes or risk factors with obesity-related health outcomes. Therefore, the range of values of moderating variables (demographic, socio-  Appendix E

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economic, and other social factors that modify the observed relationships) in models that predict outcomes is limited. The experimental evidence is even more scarce and limited in generalizability. Because of these limitations of the evidence-based practice literature, decision makers must turn to practice-based evidence and ways of pooling evidence from various extant or emerging programs and practices. Pooling refers to consultation with decision makers who have dealt with the problem of obesity in a similar population or setting. After matching and mapping the evidence and theories, local decision makers will still be uncertain about how well the evidence applies to each of the mediators (i.e., mechanisms or intermediate steps) and moderators (i.e., conditions that make an association stronger or weaker) in their logic model for local action. At this point, they should turn to the opinions of experts and experienced practitioners in their or similar settings (e.g., Banwell et al., 2005; D’Onofrio, 2001). Methods exist for pooling these opinions and analyzing them in various systematic and formal or unsystematic and informal ways. For example, Banwell and colleagues (2005) used an adapted Delphi technique (the Delphi Method, described in Chapter 6) to obtain views of obesity, dietary, and physical activity experts about social trends that have contributed to an obesogenic environment in Australia. Through this semistructured process, they were able to identify trends in expert opinion, as well as rank the trends to help inform public policy. Practice-based evidence is that which comes primarily from practice settings, in real time, and from typical practitioners, as distinct from evidence from more academ- ically controlled settings, with highly trained and supervised practitioners conducting interventions under strict protocols. Such tacit evidence, often unpublished, draws on the experience of those who have grappled with the problem and/or the intervention in situations more typical of those in which the evidence would be applied elsewhere. Even when evidence from experimental studies is available, decision makers often ask, understandably, whether it applies to their context—in their practice or policy setting, circumstances, and population (Bowen and Zwi, 2005; Dobbins et al., 2007; Dobrow et al., 2004, 2006; Green, 2008). They want to weigh what the experimental evidence shows, with its strong level of certainty of the causal relationship between the inter- vention and the observed outcomes (internal validity), against what the experience of their own and similar practices and practitioners has been, with its possibly stronger generalizability (external validity). Finally, the use of pooling in weighing and supplementing evidence becomes an important negotiating process among organizations cooperating in community-level and other broad collaborative programs and policies. Each participant in such col- laborations will weigh different types of evidence differently, and each will have an idiosyncratic view of its own experience and what it says about the problem and the proposed solutions (Best et al., 2003). This recognition of complexities in the evidence and multiplicities of experience has led to a growing interest in systems theory or sys- tems thinking (Green, 2006) (see Chapter 4). Bridging the Evidence Gap in Obesity Prevention 

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Patching Engaging people from the community affected by the problem of obesity or its deter- minants allows for the inclusion of local wisdom from the outset in the adaptation of evidence-based practices and the creation of new ideas to be tested. As with any fed- eral or state health program that must depend on local and state initiative and imple- mentation, the process of rolling out a policy or taking a program to scale requires the engagement and participation of practitioners and populations at the front lines (Ottoson et al., 2009). Success will depend on continuous adaptation to their percep- tion of needs; their understanding of and access to local resources; their willingness, skill, and confidence to implement the recommended intervention; and the reinforce- ment they will get from doing so (Ottoson and Green, 1987). Many of the methods for patching together evidence-based practices, theory-based programs, and practice- based experiences into a viable effort at the state or local level are contained in manu- als and guidelines such as CDC’s Planned Approach to Community Health (PATCH; Kreuter, 1992) and Racial and Ethnic Approaches to Community Health, (REACH; CDC, 2009b); community-based participatory research (CBPR; Cargo and Mercer, 2008; Horowitz et al., 2009; Minkler and Wallerstein, 2008); the National Cancer Institute (NCI) and Substance Abuse and Mental Health Services Administration’s (SAMHSA) Cancer Control PLANET (NCI and SAMHSA, 2009); and other web resources that need to be made more interactive and responsive as the evidence changes (e.g., http://www.cdc.gov/nutrition/professionals/researchtopractice/index.html [CDC, 2009a]). An obesity-related example of engaging community members in the planning, delivery, and evaluation of interventions is the Shape Up Somerville environmental change intervention, designed to prevent obesity in culturally diverse, high-risk early elementary school children in Somerville, Massachusetts. One outcome of this initia- tive was a decrease in BMI z-scores among children at high risk for obesity in grades 1-3, a result of an intervention that aimed to bring participants’ energy equation into balance by modifying the school, home, and community environments to increase both physical activity options and the availability of healthful foods (Economos et al., 2007). Community members and groups engaged in the intervention included chil- dren, parents, teachers, school food service providers, city departments, policy makers, health care providers, restaurants, before- and after-school programs, and the media. Another strategy of Shape Up Somerville was to improve school food service, which led to changes that enhanced the nutrient profiles of and attitudes toward school meals. The engagement of students, parents, teachers, school leaders, and food service personnel was an integral part of the process (Goldberg et al., 2009). There is also a growing literature on how to combine systematic reviews of quantitative and qualita- tive evidence with realist reviews of theoretical assumptions and with the practical experience of those who must make the final decisions on local action (Ogilvie et al., 2005). For example, Mays and colleagues (2005, p. 7) offer:  Appendix E

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• “a description of the main stages in a systematic review of evidence from research and nonresearch sources designed to inform decision making by policy makers and managers; • an indication of the range of evidence that could potentially be incorporated into such reviews; • pragmatic guidance on the main methodological issues . . . , given the early stage of development of methods of such reviews, and with a particular focus on the synthesis of qualitative and quantitative evidence; • an introduction to some of the approaches available to synthesize these different forms of evidence; and • an indication of the types of review questions particular approaches to synthesis are best able to address.” These alternatives to evidence-based practice of the most literal and rigorous scientific variety suggest some advantages and complementarities of a model of practice-based evidence that produces locally adapted and prospectively tested evidence. Users of this and other guidance for linking research to the decisions they must make in their own settings will need to trade off some degree of rigor for more reality in the setting, con- ditions of practice, and free-living populations observed. REFERENCES Abroms, L. C., and E. W. Maibach. 2008. The effectiveness of mass communication to change public behavior. Annual Review of Public Health 29:219-234. Banwell, C., S. Hinde, J. Dixon, and B. Sibthorpe. 2005. Reflections on expert consensus: A case study of the social trends contributing to obesity. European Journal of Public Health 15(6):564-568. Bartholomew, L. K., G. S. Parcel, G. Kok, and N. H. Gotleib. 2006. Planning health promotion programs: An intervention mapping approach. San Francisco, CA: Jossey-Bass Wiley. Berkman, L. F., and I. Kawachi, eds. 2000. Social epidemiology. New York: Oxford University Press. Best, A., D. Stokols, L. W. Green, S. Leischow, B. Holmes, and K. Buchholz. 2003. An integra- tive framework for community partnering to translate theory into effective health promo- tion strategy. American Journal of Health Promotion 18(2):168-176. Booth, S. L., J. F. Sallis, C. Ritenbaugh, J. O. Hill, L. L. Birch, L. D. Frank, K. Glanz, D. A. Himmelgreen, M. Mudd, B. M. Popkin, K. A. Rickard, S. St Jeor, and N. P. Hays. 2001. Environmental and societal factors affect food choice and physical activity: Rationale, influ- ences, and leverage points. Nutrition Reviews 59(3, Supplement 2):S21-S39. Bowen, S., and A. B. Zwi. 2005. Pathways to “evidence-informed” policy and practice: A framework for action. PLoS Medicine 2(7):600-605. Campbell, D. T., and D. A. Kenny. 1999. A primer on regression artifacts. New York: Guilford. Campbell, D. T., and J. C. Stanley. 1966. Experimental and quasi-experimental designs for research. Chicago, IL: Rand McNally. Bridging the Evidence Gap in Obesity Prevention 

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