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Quasi-Experimental Research Design – Types, Methods

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Quasi-Experimental Design

Quasi-experimental design is a research method that seeks to evaluate the causal relationships between variables, but without the full control over the independent variable(s) that is available in a true experimental design.

In a quasi-experimental design, the researcher uses an existing group of participants that is not randomly assigned to the experimental and control groups. Instead, the groups are selected based on pre-existing characteristics or conditions, such as age, gender, or the presence of a certain medical condition.

Types of Quasi-Experimental Design

There are several types of quasi-experimental designs that researchers use to study causal relationships between variables. Here are some of the most common types:

Non-Equivalent Control Group Design

This design involves selecting two groups of participants that are similar in every way except for the independent variable(s) that the researcher is testing. One group receives the treatment or intervention being studied, while the other group does not. The two groups are then compared to see if there are any significant differences in the outcomes.

Interrupted Time-Series Design

This design involves collecting data on the dependent variable(s) over a period of time, both before and after an intervention or event. The researcher can then determine whether there was a significant change in the dependent variable(s) following the intervention or event.

Pretest-Posttest Design

This design involves measuring the dependent variable(s) before and after an intervention or event, but without a control group. This design can be useful for determining whether the intervention or event had an effect, but it does not allow for control over other factors that may have influenced the outcomes.

Regression Discontinuity Design

This design involves selecting participants based on a specific cutoff point on a continuous variable, such as a test score. Participants on either side of the cutoff point are then compared to determine whether the intervention or event had an effect.

Natural Experiments

This design involves studying the effects of an intervention or event that occurs naturally, without the researcher’s intervention. For example, a researcher might study the effects of a new law or policy that affects certain groups of people. This design is useful when true experiments are not feasible or ethical.

Data Analysis Methods

Here are some data analysis methods that are commonly used in quasi-experimental designs:

Descriptive Statistics

This method involves summarizing the data collected during a study using measures such as mean, median, mode, range, and standard deviation. Descriptive statistics can help researchers identify trends or patterns in the data, and can also be useful for identifying outliers or anomalies.

Inferential Statistics

This method involves using statistical tests to determine whether the results of a study are statistically significant. Inferential statistics can help researchers make generalizations about a population based on the sample data collected during the study. Common statistical tests used in quasi-experimental designs include t-tests, ANOVA, and regression analysis.

Propensity Score Matching

This method is used to reduce bias in quasi-experimental designs by matching participants in the intervention group with participants in the control group who have similar characteristics. This can help to reduce the impact of confounding variables that may affect the study’s results.

Difference-in-differences Analysis

This method is used to compare the difference in outcomes between two groups over time. Researchers can use this method to determine whether a particular intervention has had an impact on the target population over time.

Interrupted Time Series Analysis

This method is used to examine the impact of an intervention or treatment over time by comparing data collected before and after the intervention or treatment. This method can help researchers determine whether an intervention had a significant impact on the target population.

Regression Discontinuity Analysis

This method is used to compare the outcomes of participants who fall on either side of a predetermined cutoff point. This method can help researchers determine whether an intervention had a significant impact on the target population.

Steps in Quasi-Experimental Design

Here are the general steps involved in conducting a quasi-experimental design:

• Identify the research question: Determine the research question and the variables that will be investigated.
• Choose the design: Choose the appropriate quasi-experimental design to address the research question. Examples include the pretest-posttest design, non-equivalent control group design, regression discontinuity design, and interrupted time series design.
• Select the participants: Select the participants who will be included in the study. Participants should be selected based on specific criteria relevant to the research question.
• Measure the variables: Measure the variables that are relevant to the research question. This may involve using surveys, questionnaires, tests, or other measures.
• Implement the intervention or treatment: Implement the intervention or treatment to the participants in the intervention group. This may involve training, education, counseling, or other interventions.
• Collect data: Collect data on the dependent variable(s) before and after the intervention. Data collection may also include collecting data on other variables that may impact the dependent variable(s).
• Analyze the data: Analyze the data collected to determine whether the intervention had a significant impact on the dependent variable(s).
• Draw conclusions: Draw conclusions about the relationship between the independent and dependent variables. If the results suggest a causal relationship, then appropriate recommendations may be made based on the findings.

Quasi-Experimental Design Examples

Here are some examples of real-time quasi-experimental designs:

• Evaluating the impact of a new teaching method: In this study, a group of students are taught using a new teaching method, while another group is taught using the traditional method. The test scores of both groups are compared before and after the intervention to determine whether the new teaching method had a significant impact on student performance.
• Assessing the effectiveness of a public health campaign: In this study, a public health campaign is launched to promote healthy eating habits among a targeted population. The behavior of the population is compared before and after the campaign to determine whether the intervention had a significant impact on the target behavior.
• Examining the impact of a new medication: In this study, a group of patients is given a new medication, while another group is given a placebo. The outcomes of both groups are compared to determine whether the new medication had a significant impact on the targeted health condition.
• Evaluating the effectiveness of a job training program : In this study, a group of unemployed individuals is enrolled in a job training program, while another group is not enrolled in any program. The employment rates of both groups are compared before and after the intervention to determine whether the training program had a significant impact on the employment rates of the participants.
• Assessing the impact of a new policy : In this study, a new policy is implemented in a particular area, while another area does not have the new policy. The outcomes of both areas are compared before and after the intervention to determine whether the new policy had a significant impact on the targeted behavior or outcome.

Applications of Quasi-Experimental Design

Here are some applications of quasi-experimental design:

• Educational research: Quasi-experimental designs are used to evaluate the effectiveness of educational interventions, such as new teaching methods, technology-based learning, or educational policies.
• Health research: Quasi-experimental designs are used to evaluate the effectiveness of health interventions, such as new medications, public health campaigns, or health policies.
• Social science research: Quasi-experimental designs are used to investigate the impact of social interventions, such as job training programs, welfare policies, or criminal justice programs.
• Business research: Quasi-experimental designs are used to evaluate the impact of business interventions, such as marketing campaigns, new products, or pricing strategies.
• Environmental research: Quasi-experimental designs are used to evaluate the impact of environmental interventions, such as conservation programs, pollution control policies, or renewable energy initiatives.

When to use Quasi-Experimental Design

Here are some situations where quasi-experimental designs may be appropriate:

• When the research question involves investigating the effectiveness of an intervention, policy, or program : In situations where it is not feasible or ethical to randomly assign participants to intervention and control groups, quasi-experimental designs can be used to evaluate the impact of the intervention on the targeted outcome.
• When the sample size is small: In situations where the sample size is small, it may be difficult to randomly assign participants to intervention and control groups. Quasi-experimental designs can be used to investigate the impact of an intervention without requiring a large sample size.
• When the research question involves investigating a naturally occurring event : In some situations, researchers may be interested in investigating the impact of a naturally occurring event, such as a natural disaster or a major policy change. Quasi-experimental designs can be used to evaluate the impact of the event on the targeted outcome.
• When the research question involves investigating a long-term intervention: In situations where the intervention or program is long-term, it may be difficult to randomly assign participants to intervention and control groups for the entire duration of the intervention. Quasi-experimental designs can be used to evaluate the impact of the intervention over time.
• When the research question involves investigating the impact of a variable that cannot be manipulated : In some situations, it may not be possible or ethical to manipulate a variable of interest. Quasi-experimental designs can be used to investigate the relationship between the variable and the targeted outcome.

Purpose of Quasi-Experimental Design

The purpose of quasi-experimental design is to investigate the causal relationship between two or more variables when it is not feasible or ethical to conduct a randomized controlled trial (RCT). Quasi-experimental designs attempt to emulate the randomized control trial by mimicking the control group and the intervention group as much as possible.

The key purpose of quasi-experimental design is to evaluate the impact of an intervention, policy, or program on a targeted outcome while controlling for potential confounding factors that may affect the outcome. Quasi-experimental designs aim to answer questions such as: Did the intervention cause the change in the outcome? Would the outcome have changed without the intervention? And was the intervention effective in achieving its intended goals?

Quasi-experimental designs are useful in situations where randomized controlled trials are not feasible or ethical. They provide researchers with an alternative method to evaluate the effectiveness of interventions, policies, and programs in real-life settings. Quasi-experimental designs can also help inform policy and practice by providing valuable insights into the causal relationships between variables.

Overall, the purpose of quasi-experimental design is to provide a rigorous method for evaluating the impact of interventions, policies, and programs while controlling for potential confounding factors that may affect the outcome.

Advantages of Quasi-Experimental Design

Quasi-experimental designs have several advantages over other research designs, such as:

• Greater external validity : Quasi-experimental designs are more likely to have greater external validity than laboratory experiments because they are conducted in naturalistic settings. This means that the results are more likely to generalize to real-world situations.
• Ethical considerations: Quasi-experimental designs often involve naturally occurring events, such as natural disasters or policy changes. This means that researchers do not need to manipulate variables, which can raise ethical concerns.
• More practical: Quasi-experimental designs are often more practical than experimental designs because they are less expensive and easier to conduct. They can also be used to evaluate programs or policies that have already been implemented, which can save time and resources.
• No random assignment: Quasi-experimental designs do not require random assignment, which can be difficult or impossible in some cases, such as when studying the effects of a natural disaster. This means that researchers can still make causal inferences, although they must use statistical techniques to control for potential confounding variables.
• Greater generalizability : Quasi-experimental designs are often more generalizable than experimental designs because they include a wider range of participants and conditions. This can make the results more applicable to different populations and settings.

Limitations of Quasi-Experimental Design

There are several limitations associated with quasi-experimental designs, which include:

• Lack of Randomization: Quasi-experimental designs do not involve randomization of participants into groups, which means that the groups being studied may differ in important ways that could affect the outcome of the study. This can lead to problems with internal validity and limit the ability to make causal inferences.
• Selection Bias: Quasi-experimental designs may suffer from selection bias because participants are not randomly assigned to groups. Participants may self-select into groups or be assigned based on pre-existing characteristics, which may introduce bias into the study.
• History and Maturation: Quasi-experimental designs are susceptible to history and maturation effects, where the passage of time or other events may influence the outcome of the study.
• Lack of Control: Quasi-experimental designs may lack control over extraneous variables that could influence the outcome of the study. This can limit the ability to draw causal inferences from the study.
• Limited Generalizability: Quasi-experimental designs may have limited generalizability because the results may only apply to the specific population and context being studied.

About the author

Muhammad Hassan

Researcher, Academic Writer, Web developer

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7.3 Quasi-Experimental Research

Learning objectives.

• Explain what quasi-experimental research is and distinguish it clearly from both experimental and correlational research.
• Describe three different types of quasi-experimental research designs (nonequivalent groups, pretest-posttest, and interrupted time series) and identify examples of each one.

The prefix quasi means “resembling.” Thus quasi-experimental research is research that resembles experimental research but is not true experimental research. Although the independent variable is manipulated, participants are not randomly assigned to conditions or orders of conditions (Cook & Campbell, 1979). Because the independent variable is manipulated before the dependent variable is measured, quasi-experimental research eliminates the directionality problem. But because participants are not randomly assigned—making it likely that there are other differences between conditions—quasi-experimental research does not eliminate the problem of confounding variables. In terms of internal validity, therefore, quasi-experiments are generally somewhere between correlational studies and true experiments.

Quasi-experiments are most likely to be conducted in field settings in which random assignment is difficult or impossible. They are often conducted to evaluate the effectiveness of a treatment—perhaps a type of psychotherapy or an educational intervention. There are many different kinds of quasi-experiments, but we will discuss just a few of the most common ones here.

Nonequivalent Groups Design

Recall that when participants in a between-subjects experiment are randomly assigned to conditions, the resulting groups are likely to be quite similar. In fact, researchers consider them to be equivalent. When participants are not randomly assigned to conditions, however, the resulting groups are likely to be dissimilar in some ways. For this reason, researchers consider them to be nonequivalent. A nonequivalent groups design , then, is a between-subjects design in which participants have not been randomly assigned to conditions.

Imagine, for example, a researcher who wants to evaluate a new method of teaching fractions to third graders. One way would be to conduct a study with a treatment group consisting of one class of third-grade students and a control group consisting of another class of third-grade students. This would be a nonequivalent groups design because the students are not randomly assigned to classes by the researcher, which means there could be important differences between them. For example, the parents of higher achieving or more motivated students might have been more likely to request that their children be assigned to Ms. Williams’s class. Or the principal might have assigned the “troublemakers” to Mr. Jones’s class because he is a stronger disciplinarian. Of course, the teachers’ styles, and even the classroom environments, might be very different and might cause different levels of achievement or motivation among the students. If at the end of the study there was a difference in the two classes’ knowledge of fractions, it might have been caused by the difference between the teaching methods—but it might have been caused by any of these confounding variables.

Of course, researchers using a nonequivalent groups design can take steps to ensure that their groups are as similar as possible. In the present example, the researcher could try to select two classes at the same school, where the students in the two classes have similar scores on a standardized math test and the teachers are the same sex, are close in age, and have similar teaching styles. Taking such steps would increase the internal validity of the study because it would eliminate some of the most important confounding variables. But without true random assignment of the students to conditions, there remains the possibility of other important confounding variables that the researcher was not able to control.

Pretest-Posttest Design

In a pretest-posttest design , the dependent variable is measured once before the treatment is implemented and once after it is implemented. Imagine, for example, a researcher who is interested in the effectiveness of an antidrug education program on elementary school students’ attitudes toward illegal drugs. The researcher could measure the attitudes of students at a particular elementary school during one week, implement the antidrug program during the next week, and finally, measure their attitudes again the following week. The pretest-posttest design is much like a within-subjects experiment in which each participant is tested first under the control condition and then under the treatment condition. It is unlike a within-subjects experiment, however, in that the order of conditions is not counterbalanced because it typically is not possible for a participant to be tested in the treatment condition first and then in an “untreated” control condition.

If the average posttest score is better than the average pretest score, then it makes sense to conclude that the treatment might be responsible for the improvement. Unfortunately, one often cannot conclude this with a high degree of certainty because there may be other explanations for why the posttest scores are better. One category of alternative explanations goes under the name of history . Other things might have happened between the pretest and the posttest. Perhaps an antidrug program aired on television and many of the students watched it, or perhaps a celebrity died of a drug overdose and many of the students heard about it. Another category of alternative explanations goes under the name of maturation . Participants might have changed between the pretest and the posttest in ways that they were going to anyway because they are growing and learning. If it were a yearlong program, participants might become less impulsive or better reasoners and this might be responsible for the change.

Another alternative explanation for a change in the dependent variable in a pretest-posttest design is regression to the mean . This refers to the statistical fact that an individual who scores extremely on a variable on one occasion will tend to score less extremely on the next occasion. For example, a bowler with a long-term average of 150 who suddenly bowls a 220 will almost certainly score lower in the next game. Her score will “regress” toward her mean score of 150. Regression to the mean can be a problem when participants are selected for further study because of their extreme scores. Imagine, for example, that only students who scored especially low on a test of fractions are given a special training program and then retested. Regression to the mean all but guarantees that their scores will be higher even if the training program has no effect. A closely related concept—and an extremely important one in psychological research—is spontaneous remission . This is the tendency for many medical and psychological problems to improve over time without any form of treatment. The common cold is a good example. If one were to measure symptom severity in 100 common cold sufferers today, give them a bowl of chicken soup every day, and then measure their symptom severity again in a week, they would probably be much improved. This does not mean that the chicken soup was responsible for the improvement, however, because they would have been much improved without any treatment at all. The same is true of many psychological problems. A group of severely depressed people today is likely to be less depressed on average in 6 months. In reviewing the results of several studies of treatments for depression, researchers Michael Posternak and Ivan Miller found that participants in waitlist control conditions improved an average of 10 to 15% before they received any treatment at all (Posternak & Miller, 2001). Thus one must generally be very cautious about inferring causality from pretest-posttest designs.

Does Psychotherapy Work?

Early studies on the effectiveness of psychotherapy tended to use pretest-posttest designs. In a classic 1952 article, researcher Hans Eysenck summarized the results of 24 such studies showing that about two thirds of patients improved between the pretest and the posttest (Eysenck, 1952). But Eysenck also compared these results with archival data from state hospital and insurance company records showing that similar patients recovered at about the same rate without receiving psychotherapy. This suggested to Eysenck that the improvement that patients showed in the pretest-posttest studies might be no more than spontaneous remission. Note that Eysenck did not conclude that psychotherapy was ineffective. He merely concluded that there was no evidence that it was, and he wrote of “the necessity of properly planned and executed experimental studies into this important field” (p. 323). You can read the entire article here:

http://psychclassics.yorku.ca/Eysenck/psychotherapy.htm

Fortunately, many other researchers took up Eysenck’s challenge, and by 1980 hundreds of experiments had been conducted in which participants were randomly assigned to treatment and control conditions, and the results were summarized in a classic book by Mary Lee Smith, Gene Glass, and Thomas Miller (Smith, Glass, & Miller, 1980). They found that overall psychotherapy was quite effective, with about 80% of treatment participants improving more than the average control participant. Subsequent research has focused more on the conditions under which different types of psychotherapy are more or less effective.

In a classic 1952 article, researcher Hans Eysenck pointed out the shortcomings of the simple pretest-posttest design for evaluating the effectiveness of psychotherapy.

Wikimedia Commons – CC BY-SA 3.0.

Interrupted Time Series Design

A variant of the pretest-posttest design is the interrupted time-series design . A time series is a set of measurements taken at intervals over a period of time. For example, a manufacturing company might measure its workers’ productivity each week for a year. In an interrupted time series-design, a time series like this is “interrupted” by a treatment. In one classic example, the treatment was the reduction of the work shifts in a factory from 10 hours to 8 hours (Cook & Campbell, 1979). Because productivity increased rather quickly after the shortening of the work shifts, and because it remained elevated for many months afterward, the researcher concluded that the shortening of the shifts caused the increase in productivity. Notice that the interrupted time-series design is like a pretest-posttest design in that it includes measurements of the dependent variable both before and after the treatment. It is unlike the pretest-posttest design, however, in that it includes multiple pretest and posttest measurements.

Figure 7.5 “A Hypothetical Interrupted Time-Series Design” shows data from a hypothetical interrupted time-series study. The dependent variable is the number of student absences per week in a research methods course. The treatment is that the instructor begins publicly taking attendance each day so that students know that the instructor is aware of who is present and who is absent. The top panel of Figure 7.5 “A Hypothetical Interrupted Time-Series Design” shows how the data might look if this treatment worked. There is a consistently high number of absences before the treatment, and there is an immediate and sustained drop in absences after the treatment. The bottom panel of Figure 7.5 “A Hypothetical Interrupted Time-Series Design” shows how the data might look if this treatment did not work. On average, the number of absences after the treatment is about the same as the number before. This figure also illustrates an advantage of the interrupted time-series design over a simpler pretest-posttest design. If there had been only one measurement of absences before the treatment at Week 7 and one afterward at Week 8, then it would have looked as though the treatment were responsible for the reduction. The multiple measurements both before and after the treatment suggest that the reduction between Weeks 7 and 8 is nothing more than normal week-to-week variation.

Figure 7.5 A Hypothetical Interrupted Time-Series Design

The top panel shows data that suggest that the treatment caused a reduction in absences. The bottom panel shows data that suggest that it did not.

Combination Designs

A type of quasi-experimental design that is generally better than either the nonequivalent groups design or the pretest-posttest design is one that combines elements of both. There is a treatment group that is given a pretest, receives a treatment, and then is given a posttest. But at the same time there is a control group that is given a pretest, does not receive the treatment, and then is given a posttest. The question, then, is not simply whether participants who receive the treatment improve but whether they improve more than participants who do not receive the treatment.

Imagine, for example, that students in one school are given a pretest on their attitudes toward drugs, then are exposed to an antidrug program, and finally are given a posttest. Students in a similar school are given the pretest, not exposed to an antidrug program, and finally are given a posttest. Again, if students in the treatment condition become more negative toward drugs, this could be an effect of the treatment, but it could also be a matter of history or maturation. If it really is an effect of the treatment, then students in the treatment condition should become more negative than students in the control condition. But if it is a matter of history (e.g., news of a celebrity drug overdose) or maturation (e.g., improved reasoning), then students in the two conditions would be likely to show similar amounts of change. This type of design does not completely eliminate the possibility of confounding variables, however. Something could occur at one of the schools but not the other (e.g., a student drug overdose), so students at the first school would be affected by it while students at the other school would not.

Finally, if participants in this kind of design are randomly assigned to conditions, it becomes a true experiment rather than a quasi experiment. In fact, it is the kind of experiment that Eysenck called for—and that has now been conducted many times—to demonstrate the effectiveness of psychotherapy.

Key Takeaways

• Quasi-experimental research involves the manipulation of an independent variable without the random assignment of participants to conditions or orders of conditions. Among the important types are nonequivalent groups designs, pretest-posttest, and interrupted time-series designs.
• Quasi-experimental research eliminates the directionality problem because it involves the manipulation of the independent variable. It does not eliminate the problem of confounding variables, however, because it does not involve random assignment to conditions. For these reasons, quasi-experimental research is generally higher in internal validity than correlational studies but lower than true experiments.
• Practice: Imagine that two college professors decide to test the effect of giving daily quizzes on student performance in a statistics course. They decide that Professor A will give quizzes but Professor B will not. They will then compare the performance of students in their two sections on a common final exam. List five other variables that might differ between the two sections that could affect the results.

Discussion: Imagine that a group of obese children is recruited for a study in which their weight is measured, then they participate for 3 months in a program that encourages them to be more active, and finally their weight is measured again. Explain how each of the following might affect the results:

• regression to the mean
• spontaneous remission

Cook, T. D., & Campbell, D. T. (1979). Quasi-experimentation: Design & analysis issues in field settings . Boston, MA: Houghton Mifflin.

Eysenck, H. J. (1952). The effects of psychotherapy: An evaluation. Journal of Consulting Psychology, 16 , 319–324.

Posternak, M. A., & Miller, I. (2001). Untreated short-term course of major depression: A meta-analysis of studies using outcomes from studies using wait-list control groups. Journal of Affective Disorders, 66 , 139–146.

Smith, M. L., Glass, G. V., & Miller, T. I. (1980). The benefits of psychotherapy . Baltimore, MD: Johns Hopkins University Press.

Research Methods in Psychology Copyright © 2016 by University of Minnesota is licensed under a Creative Commons Attribution-NonCommercial-ShareAlike 4.0 International License , except where otherwise noted.

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Quasi-Experimental Design

• Usability Studies

Quasi-Experimental Design is a unique research methodology because it is characterized by what is lacks. For example, Abraham & MacDonald (2011) state:

" Quasi-experimental research is similar to experimental research in that there is manipulation of an independent variable. It differs from experimental research because either there is no control group, no random selection, no random assignment, and/or no active manipulation. "

This type of research is often performed in cases where a control group cannot be created or random selection cannot be performed. This is often the case in certain medical and psychological studies. 

For more information on quasi-experimental design, review the resources below: 

Where to Start

Below are listed a few tools and online guides that can help you start your Quasi-experimental research. These include free online resources and resources available only through ISU Library.

• Quasi-Experimental Research Designs by Bruce A. Thyer This pocket guide describes the logic, design, and conduct of the range of quasi-experimental designs, encompassing pre-experiments, quasi-experiments making use of a control or comparison group, and time-series designs. An introductory chapter describes the valuable role these types of studies have played in social work, from the 1930s to the present. Subsequent chapters delve into each design type's major features, the kinds of questions it is capable of answering, and its strengths and limitations.
• Experimental and Quasi-Experimental Designs for Research by Donald T. Campbell; Julian C. Stanley. Call Number: Q175 C152e Written 1967 but still used heavily today, this book examines research designs for experimental and quasi-experimental research, with examples and judgments about each design's validity.

Online Resources

• Quasi-Experimental Design From the Web Center for Social Research Methods, this is a very good overview of quasi-experimental design.
• Experimental and Quasi-Experimental Research From Colorado State University.
• Quasi-experimental design--Wikipedia, the free encyclopedia Wikipedia can be a useful place to start your research- check the citations at the bottom of the article for more information.
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Selecting and Improving Quasi-Experimental Designs in Effectiveness and Implementation Research

Margaret a. handley.

1 Department of Epidemiology and Biostatistics, Division of Infectious Disease Epidemiology, University of California, San Francisco, CA

2 General Internal Medicine and UCSF Center for Vulnerable Populations, San Francisco Zuckerberg General Hospital and Trauma Center, University of California, San Francisco, CA, 1001 Potrero Avenue, Box 1364, San Francisco, CA 94110

Courtney Lyles

Charles mcculloch, adithya cattamanchi.

3 Division of Pulmonary and Critical Care Medicine and UCSF Center for Vulnerable Populations, San Francisco Zuckerberg General Hospital and Trauma Center, University of California, San Francisco, CA, 1001 Potrero Avenue, San Francisco, CA 94110

Interventional researchers face many design challenges when assessing intervention implementation in real-world settings. Intervention implementation requires ‘holding fast’ on internal validity needs while incorporating external validity considerations (such as uptake by diverse sub-populations, acceptability, cost, sustainability). Quasi-experimental designs (QEDs) are increasingly employed to achieve a better balance between internal and external validity. Although these designs are often referred to and summarized in terms of logistical benefits versus threats to internal validity, there is still uncertainty about: (1) how to select from among various QEDs, and (2) strategies to strengthen their internal and external validity. We focus on commonly used QEDs (pre-post designs with non-equivalent control groups, interrupted time series, and stepped wedge designs) and discuss several variants that maximize internal and external validity at the design, execution, and analysis stages.

INTRODUCTION

Public health practice involves implementation or adaptation of evidence-based interventions into new settings in order to improve health for individuals and populations. Such interventions typically include on one or more of the “7 Ps” (programs, practices, principles, procedures, products, pills, and policies) ( 9 ). Increasingly, both public health and clinical research have sought to generate practice-based evidence on a wide range of interventions, which in turn has led to a greater focus on intervention research designs that can be applied in real-world settings ( 2 , 8 , 9 , 20 , 25 , 26 , 10 , 2 ).

Randomized controlled trials (RCTs) in which individuals are assigned to intervention or control (standard-of-care or placebo) arms are considered the gold standard for assessing causality and as such are a first choice for most intervention research. Random allocation minimizes selection bias and maximizes the likelihood that measured and unmeasured confounding variables are distributed equally, enabling any difference in outcomes between intervention and control arms to be attributed to the intervention under study. RCTs can also involve random assignment of groups (e.g., clinics, worksites or communities) to intervention and control arms, but a large number of groups are required in order to realize the full benefits of randomization. Traditional RCTs strongly prioritize internal validity over external validity by employing strict eligibility criteria and rigorous data collection methods.

Alternative research methods are needed to test interventions for their effectiveness in many real-world settings—and later when evidence-based interventions are known, for spreading or scaling up these interventions to new settings and populations ( 23 , 40 ). In real-world settings, random allocation of the intervention may not be possible or fully under the control of investigators because of practical, ethical, social, or logistical constraints. For example, when partnering with communities or organizations to deliver a public health intervention, it might not be acceptable that only half of individuals or sites receive an intervention. As well, the timing of intervention roll-out might be determined by an external process outside the control of the investigator, such as a mandated policy. Also, when self-selected groups are expected to participate in a program as part of routine care, there would arise ethical concerns associated with random assignment – for example, the withholding or delaying of a potentially effective treatment or the provision of a less effective treatment for one group of participants ( 49 ). As described by Peters et al “implementation research seeks to understand and work within real world conditions, rather than trying to control for these conditions or to remove their influence as causal effects. “ ( 40 ). For all of these reasons, a blending of the design components of clinical effectiveness trials and implementation research is feasible and desirable, and this review covers both. Such blending of effectiveness and implementation components within a study can provide benefits beyond either research approach alone ( 14 ), for example by leading to faster uptake of interventions by simultaneously testing implementation strategies.

Since assessment of intervention effectiveness and implementation in real-world settings requires increased focus on external validity (including consideration of factors enhancing intervention uptake by diverse sub-populations, acceptability to a wide range of stakeholders, cost, and sustainability) ( 34 ), interventional research designs are needed that are more relevant to the potential, ‘hoped for’ treatment population than a RCT, and that achieve a better balance between internal and external validity. Quasi-experimental designs (QEDs), which first gained prominence in social science research ( 11 ), are increasingly being employed to fill this need. [ BOX 1 HERE: Definitions used in this review].

DEFINITIONS AND TERMS USED IN PAPER

QEDs test causal hypotheses but, in lieu of fully randomized assignment of the intervention, seek to define a comparison group or time period that reflects the counter-factual ( i.e., outcomes if the intervention had not been implemented) ( 43 ). QEDs seek to identify a comparison group or time period that is as similar as possible to the treatment group or time period in terms of baseline (pre-intervention) characteristics. QEDs can include partial randomization such as in stepped wedge designs (SWD) when there is pre-determined (and non-random) stratification of sites, but the order in which sites within each strata receive the intervention is assigned randomly. For example, strata that are determined by size or perceived ease of implementation may be assigned to receive the intervention first. However, within those strata the specific sites themselves are randomly selected to receive the intervention across the time intervals included in the study). In all cases, the key threat to internal validity of QEDs is a lack of similarity between the comparison and intervention groups or time periods due to differences in characteristics of the people, sites, or time periods involved.

Previous reviews in this journal have focused on the importance and use of QEDs and other methods to enhance causal inference when evaluating the impact of an intervention that has already been implemented ( 4 , 8 , 9 , 18 ). Design approaches in this case often include creating a post-hoc comparison group for a natural experiment or identifying pre and post-intervention data to then conduct an interrupted time series study. Analysis phase approaches often utilize techniques such as pre-post, regression adjustment, scores, difference-in-differences, synthetic controls, interrupted time series, regression discontinuity, and instrumental variables ( 4 , 9 , 18 ). Although these articles summarize key components of QEDs (e.g. interrupted time series), as well as analysis-focused strategies (regression adjustment, propensity scores, difference-in-differences, synthetic controls, and instrumental variables) there is still uncertainty about: (1) how to select from among various QEDs in the pre-implementation design phase, and (2) strategies to strengthen internal and external validity before and during the implementation phase.

In this paper we discuss the a priori choice of a QED when evaluating the impact of an intervention or policy for which the investigator has some element of design control related to 1) order of intervention allocation (including random and non-random approaches); 2) selecting sites or individuals; and/or 3) timing and frequency of data collection. In the next section, we discuss the main QEDs used for prospective evaluations of interventions in real-world settings and their advantages and disadvantages with respect to addressing threats to internal validity [ BOX 2 HERE Common Threats to Internal Validty of Quasi-Experimental Designs Evaluating Interventions in ‘Real World’ Settings]. Following this summary, we discuss opportunities to strengthen their internal validity, illustrated with examples from the literature. Then we propose a decision framework for key decision points that lead to different QED options. We conclude with a brief discussion of incorporating additional design elements to capture the full range of relevant implementation outcomes in order to maximize external validity.

Common Threats to Internal Validty of Quasi-Experimental Designs Evaluating Interventions in ‘Real World’ Settings

QUASI-EXPERIMENTAL DESIGNS FOR PROSPECTIVE EVALUTION OF INTERVENTIONS

Table 1 summarizes the main QEDs that have been used for prospective evaluation of health intervention in real-world settings; pre-post designs with a non-equivalent control group, interrupted time series and stepped wedge designs. We do not include pre-post designs without a control group in this review, as in general, QEDs are primarily those designs that identify a comparison group or time period that is as similar as possible to the treatment group or time period in terms of baseline (pre-intervention) characteristics ( 50 ). Below, we describe features of each QED, considering strengths and limitations and providing examples of their use.

Overview of Commonly Used QED in Intervention Research*

1. Pre-Post With Non-Equivalent Control Group

The first type of QED highlighted in this review is perhaps the most straightforward type of intervention design: the pre-post comparison study with a non-equivalent control group. In this design, the intervention is introduced at a single point in time to one or more sites, for which there is also a pre-test and post-test evaluation period, The pre-post differences between these two sites is then compared. In practice, interventions using this design are often delivered at a higher level, such as to entire communities or organizations 1 [ Figure 1 here]. In this design the investigators identify additional site(s) that are similar to the intervention site to serve as a comparison/control group. However, these control sites are different in some way than the intervention site(s) and thus the term “non-equivalent” is important, and clarifies that there are inherent differences in the treatment and control groups ( 15 ).

Illustration of the Pre-Post Non-Equivalent Control Group Design

The strengths of pre-post designs are mainly based in their simplicity, such as data collection is usually only at a few points (although sometimes more). However, pre-post designs can be affected by several of the threats to internal validity of QEDs presented here. The largest challenges are related to 1) ‘history bias’ in which events unrelated to the intervention occur (also referred to as secular trends) before or during the intervention period and have an effect on the outcome (either positive or negative) that are not related to the intervention ( 39 ); and 2) differences between the intervention and control sites because the non-equivalent control groups are likely to differ from the intervention sites in a number of meaningful ways that impact the outcome of interest and can bias results (selection bias).

At this design stage, the first step at improving internal validity would be focused on selection of a non-equivalent control group(s) for which some balance in the distribution of known risk factors is established. This can be challenging as there may not be adequate information available to determine how ‘equivalent’ the comparison group is regarding relevant covariates.

It can be useful to obtain pre-test data or baseline characteristics to improve the comparability of the two groups. In the most controlled situations within this design, the investigators might include elements of randomization or matching for individuals in the intervention or comparison site, to attempt to balance the covariate distribution. Implicit in this approach is the assumption that the greater the similarity between groups, the smaller the likelihood that confounding will threaten inferences of causality of effect for the intervention ( 33 , 47 ). Thus, it is important to select this group or multiple groups with as much specificity as possible.

In order to enhance the causal inference for pre-post designs with non-equivalent control groups, the best strategies improve the comparability of the control group with regards to potential covariates related to the outcome of interest but are not under investigation. One strategy involves creating a cohort, and then using targeted sampling to inform matching of individuals within the cohort. Matching can be based on demographic and other important factors (e.g. measures of health care access or time-period). This design in essence creates a matched, nested case-control design.

Collection of additional data once sites are selected cannot in itself reduce bias, but can inform the examination of the association of interest, and provide data supporting interpretation consistent with the reduced likelihood of bias. These data collection strategies include: 1) extra data collection points at additional pre- or post- time points (to get closer to an interrupted time series design in effect and examine potential threats of maturation and history bias), and 2) collection of data on other dependent variables with a priori assessment of how they will ‘react’ with time dependent variables. A detailed analysis can then provide information on the potential affects on the outcome of interest (to understand potential underlying threats due to history bias).

Additionally, there are analytic strategies that can improve the interpretation of this design, such as: 1) analysis for multiple non-equivalent control groups, to determine if the intervention effects are robust across different conditions or settings (.e.g. using sensitivity analysis), 2) examination within a smaller critical window of the study in which the intervention would be plausibly expected to make the most impact, and 3) identification of subgroups of individuals within the intervention community who are known to have received high vs. low exposure to the intervention, to be able to investigate a potential “dose-response” effect. Table 2 provides examples of studies using the pre-post non-equivalent control group designs that have employed one or more of these improvement approaches to improve the internal study’s validity.

Improving Quasi-Experimental Designs-Internal and External Validity Considerations

Cousins et al utilized a non-equivalent control selection strategy to leverage a recent cross-sectional survey among six universities in New Zealand regarding drinking among college-age students ( 16 ). In the original survey, there were six sites, and for the control group, five were selected to provide non-equivalent control group data for the one intervention campus. The campus intervention targeted young adult drinking-related problems and other outcomes, such as aggressive behavior, using an environmental intervention with a community liaison and a campus security program (also know as a Campus Watch program). The original cross-sectional survey was administered nationally to students using a web-based format, and was repeated in the years soon after the Campus Watch intervention was implemented in one site. Benefits of the design include: a consistent sampling frame at each control sites, such that sites could be combined as well as evaluated separately and collection of additional data on alcohol sales and consumption over the study period, to support inference. In a study by Wertz et al ( 48 ), a non-equivalent control group was created using matching for those who were eligible for a health coaching program and opted out of the program (to be compared with those who opted in) among insured patients with diabetes and/or hypertension. Matching was based on propensity scores among those patients using demographic and socioeconomic factors and medical center location and a longitudinal cohort was created prior to the intervention (see Basu et al 2017 for more on this approach).

In the pre-post malaria-prevention intervention example from Gambia, the investigators were studying the introduction of bed nets treated with insecticide on malaria rates in Gambia, and collected additional data to evaluate the internal validity assumptions within their design ( 1 ). In this study, the investigators introduced bed nets at the village level, using communities not receiving the bed nets as control sites. To strengthen the internal validity they collected additional data that enabled them to: 1) determine whether the reduction in malaria rates were most pronounced during the rainy season within the intervention communities, as this was a biologically plausible exposure period in which they could expect the largest effect size difference between intervention and control sites, and 2) examine use patterns for the bed nets, based on how much insecticide was present in the bed nets over time (after regular washing occurred), which aided in calculating a “dose-response” effect of exposure to the bed net among a subsample of individuals in the intervention community.

2. Interrupted Time Series

An interrupted time series (ITS) design involves collection of outcome data at multiple time points before and after an intervention is introduced at a given point in time at one or more sites ( 6 , 13 ). The pre-intervention outcome data is used to establish an underlying trend that is assumed to continue unchanged in the absence of the intervention under study ( i.e., the counterfactual scenario). Any change in outcome level or trend from the counter-factual scenario in the post-intervention period is then attributed to the impact of the intervention. The most basic ITS design utilizes a regression model that includes only three time-based covariates to estimate the pre-intervention slope (outcome trend before the intervention), a “step” or change in level (difference between observed and predicted outcome level at the first post-intervention time point), and a change in slope (difference between post- and pre-intervention outcome trend) ( 13 , 32 ) [ Figure 2 here].

Interrupted Time Series Design

Whether used for evaluating a natural experiment or, as is the focus here, for prospective evaluation of an intervention, the appropriateness of an ITS design depends on the nature of the intervention and outcome, and the type of data available. An ITS design requires the pre- and post-intervention periods to be clearly differentiated. When used prospectively, the investigator therefore needs to have control over the timing of the intervention. ITS analyses typically involve outcomes that are expected to change soon after an intervention is introduced or after a well-defined lag period. For example, for outcomes such as cancer or incident tuberculosis that develop long after an intervention is introduced and at a variable rate, it is difficult to clearly separate the pre- and post-intervention periods. Last, an ITS analysis requires at least three time points in the pre- and post-intervention periods to assess trends. In general, a larger number of time points is recommended, particularly when the expected effect size is smaller, data are more similar at closer together time points ( i.e., auto-correlation), or confounding effects ( e.g., seasonality) are present. It is also important for investigators to consider any changes to data collection or recording over time, particularly if such changes are associated with introduction of the intervention.

In comparison to simple pre-post designs in which the average outcome level is compared between the pre- and post-intervention periods, the key advantage of ITS designs is that they evaluate for intervention effect while accounting for pre-intervention trends. Such trends are common due to factors such as changes in the quality of care, data collection and recording, and population characteristics over time. In addition, ITS designs can increase power by making full use of longitudinal data instead of collapsing all data to single pre- and post-intervention time points. The use of longitudinal data can also be helpful for assessing whether intervention effects are short-lived or sustained over time.

While the basic ITS design has important strengths, the key threat to internal validity is the possibility that factors other than the intervention are affecting the observed changes in outcome level or trend. Changes over time in factors such as the quality of care, data collection and recording, and population characteristics may not be fully accounted for by the pre-intervention trend. Similarly, the pre-intervention time period, particularly when short, may not capture seasonal changes in an outcome.

Detailed reviews have been published of variations on the basic ITS design that can be used to enhance causal inference. In particular, the addition of a control group can be particularly useful for assessing for the presence of seasonal trends and other potential time-varying confounders ( 52 ). Zombre et al ( 52 ) maintained a large number of control number of sites during the extended study period and were able to look at variations in seasonal trends as well as clinic-level characteristics, such as workforce density and sustainability. In addition to including a control group, several analysis phase strategies can be employed to strengthen causal inference including adjustment for time varying confounders and accounting for auto correlation.

3. Stepped Wedge Designs

Stepped wedge designs (SWDs) involve a sequential roll-out of an intervention to participants (individuals or clusters) over several distinct time periods ( 5 , 7 , 22 , 24 , 29 , 30 , 38 ). SWDs can include cohort designs (with the same individuals in each cluster in the pre and post intervention steps), and repeated cross-sectional designs (with different individuals in each cluster in the pre and post intervention steps) ( 7 ). In the SWD, there is a unidirectional, sequential roll- out of an intervention to clusters (or individuals) that occurs over different time periods. Initially all clusters (or individuals) are unexposed to the intervention, and then at regular intervals, selected clusters cross over (or ‘step’) into a time period where they receive the intervention [ Figure 3 here]. All clusters receive the intervention by the last time interval (although not all individuals within clusters necessarily receive the intervention). Data is collected on all clusters such that they each contribute data during both control and intervention time periods. The order in which clusters receive the intervention can be assigned randomly or using some other approach when randomization is not possible. For example, in settings with geographically remote or difficult-to-access populations, a non-random order can maximize efficiency with respect to logistical considerations.

Illustration of the stepped wedge study design-Intervention Roll-Out Over Time*

* Adapted from Turner et al 2017

The practical and social benefits of the stepped wedge design have been summarized in recent reviews ( 5 , 22 , 24 , 27 , 29 , 36 , 38 , 41 , 42 , 45 , 46 , 51 ). In addition to addressing general concerns with RCTs discussed earlier, advantages of SWDs include the logistical convenience of staggered roll-out of the intervention, which enables a.smaller staff to be distributed across different implementation start times and allows for multi-level interventions to be integrated into practice or ‘real world’ settings (referred to as the feasibility benefit). This benefit also applies to studies of de-implementation, prior to a new approach being introduced. For example, with a staggered roll-out it is possible to build in a transition cohort, such that sites can adjust to the integration of the new intervention, and also allow for a switching over in sites to de-implementing a prior practice. For a specified time period there may be ‘mixed’ or incomplete data, which can be excluded from the data analysis. However, associated with a longer duration of roll-out for practical reasons such as this switching, are associated costs in threats to internal validity, discussed below.

There are several limitations to the SWD. These generally involve consequences of the trade-offs related to having design control for the intervention roll-out, often due to logistical reasons on the one hand, but then having ‘down the road’ threats to internal validity. These roll-out related threats include potential lagged intervention effects for non-acute outcomes; possible fatigue and associated higher drop-out rates of waiting for the cross-over among clusters assigned to receive the intervention later; fidelity losses for key intervention components over time; and potential contamination of later clusters ( 22 ). Another drawback of the SWD is that it involves data assessment at each point when a new cluster receives the intervention, substantially increasing the burden of data collection and costs unless data collection can be automated or uses existing data sources. Because the SWD often has more clusters receiving the intervention towards the end of the intervention period than in previous time periods, there is a potential concern that there can be temporal confounding at this stage. The SWD is also not as suited for evaluating intervention effects on delayed health outcomes (such as chronic disease incidence), and is most appropriate when outcomes that occur relatively soon after each cluster starts receiving the intervention. Finally, as logistical necessity often dictates selecting a design with smaller numbers of clusters, there are relatedly challenges in the statistical analysis. To use standard software, the common recommendation is to have at least 20 to 30 clusters ( 35 ).

Stepped wedge designs can embed improvements that can enhance internal validity, mimicking the strength of RCTs. These generally focus on efforts to either reduce bias or achieve balance in covariates across sites and over time; and/or compensate as much as possible for practical decisions made at the implementation stage, which affect the distribution of the intervention over time and by sites. The most widely used approaches are discussed in order of benefit to internal validity: 1) partial randomization; 2) stratification and matching; 3) embedding data collection at critical points in time, such as with a phasing-in of intervention components, and 4) creating a transition cohort or wash-out period. The most important of these SWD elements is random assignment of clusters as to when they will cross over into the intervention period. As well, utilizing data regarding time-varying covariates/confounders, either to stratify clusters and then randomize within strata (partial randomization) or to match clusters on known covariates in the absence of randomization, are techniques often employed to minimize bias and reduce confounding. Finally, maintaining control over the number and timing of data collection points over the study period can be beneficial in several ways. First, it can allow for data analysis strategies that can incorporate cyclical temporal trends (such as seasonality-mediated risk for the outcome, such as with flu or malaria) or other underlying temporal trends. Second, it can enable phased interventions to be studied for the contribution of different components included in the phases (e.g. passive then active intervention components), or can enable ‘pausing’ time, as when there is a structured wash out or transition cohort created for practical reasons (e.g. one intervention or practice is stopped/de-implemented, and a new one is introduced) (see Figure 4 ).

Illustration of the stepped wedge study design- Summary of Exposed and Unexposed Cluster Time*

Adapted from Hemming 2015

Table 2 provides examples of studies using SWD that have used one or more of the design approaches described above to improve the internal validity of the study. In the study by Killam et al 2010 ( 31 ), a non-randomized SWD was used to evaluate a complex clinic-based intervention for integrating anti-retro viral (ART) treatment into routine antenatal care in Zambia for post-partum women. The design involved matching clinics by size and an inverse roll-out, to balance out the sizes across the four groups. The inverse roll-out involved four strata of clinics, grouped by size with two clinics in each strata. The roll-out was sequenced across these eight clinics, such that one smaller clinics began earlier, with three clinics of increasing size getting the intervention afterwards. This was then followed by a descending order of clinics by size for the remaining roll-out, ending with the smallest clinic. This inverse roll-out enabled the investigators to start with a smaller clinic, to work out the logistical considerations, but then influence the roll-out such as to avoid clustering of smaller or larger clinics in any one step of the intervention.

A second design feature of this study involved the use of a transition cohort or wash-out period (see Figure 4 ) (also used in the Morrison et al 2015 study)( 19 , 37 ). This approach can be used when an existing practice is being replaced with the new intervention, but there is ambiguity as to which group an individual would be assigned to while integration efforts were underway. In the Killam study, the concern was regarding women who might be identified as ART-eligible in the control period but actually enroll into and initiate ART at an antenatal clinic during the intervention period. To account for the ambiguity of this transition period, patients with an initial antenatal visit more than 60 days prior to the date of implementing the ART in the intervention sites were excluded. For analysis of the primary outcome, patients were categorized into three mutually exclusive categories: a referral to ART cohort, an integrated ART in the antenatal clinics cohort, and a transition cohort. It is important to note that the time period for a transition cohort can add considerable time to an intervention roll-out, especially when there is to be a de-implementation of an existing practice that involves a wide range or staff or activities. As well, the exclusion of the data during this phase can reduce the study’s power if not built into the sample size considerations at the design phase.

Morrison et al 2015 ( 37 ) used a randomized cluster design, with additional stratification and randomization within relevant sub-groups to examine a two-part quality improvement intervention focusing on clinician uptake of patient cooling procedures for post-cardiac care in hospital settings (referred to as Targeted Temperature Management). In this study, 32 hospitals were stratified into two groups based on intensive care unit size (< 10 beds vs ≥ 10 beds), and then randomly assigned into four different time periods to receive the intervention. The phased intervention implementation included both passive (generic didactic training components regarding the intervention) and an active (tailored support to site-specific barriers identified in passive phase) components. This study exemplifies some of the best uses of SWD in the context of QI interventions that have either multiple components of for which there may be a passive and active phase, as is often the case with interventions that are layered onto systems change requirements (e.g. electronic records improvements/customization) or relate to sequenced guidelines implementation (as in this example).

Studies using a wait-list partial randomization design are also included in Table 2 ( 24 , 27 , 42 ). These types of studies are well-suited to settings where there is routine enumeration of a cohort based on a specific eligibility criteria, such as enrolment in a health plan or employment group, or from a disease-based registry, such as for diabetes ( 27 , 42 ). It has also been reported that this design can increase efficiency and statistical power in contrast to cluster-based trials, a crucial consideration when the number of participating individuals or groups is small ( 22 ).

The study by Grant et al et al uses a variant of the SWD for which individuals within a setting are enumerated and then randomized to get the intervention. In this example, employees who had previously screened positive for HIV at the company clinic as part of mandatory testing, were invited in random sequence to attend a workplace HIV clinic at a large mining facility in South Africa to initiate a preventive treatment for TB during the years prior to the time when ARTs were more widely available. Individuals contributed follow-up time to the “pre-clinic” phase from the baseline date established for the cohort until the actual date of their first clinic visit, and also to the “post- clinic” phase thereafter. Clinic visits every 6 months were used to identify incident TB events. Because they were looking at reduction in TB incidence among the workers at the mine and not just those in the study, the effect of the intervention (the provision of clinic services) was estimated for the entire study population (incidence rate ratio), irrespective of whether they actually received isoniazid.

CONSIDERATIONS IN CHOOSING BETWEEN QED

We present a decision ‘map’ approach based on a Figure 5 to assist in considering decisions in selecting among QEDs and for which features you can pay particular attention to in the design [ Figure 5 here].

Quasi-Experimental Design Decision-Making Map

First, at the top of the flow diagram ( 1 ), consider if you can have multiple time points you can collect data for in the pre and post intervention periods. Ideally, you will be able to select more than two time points. If you cannot, then multiple sites would allow for a non-equivalent pre-post design. If you can have more than the two time points for the study assessments, you next need to determine if you can include multiple sites ( 2 ). If not, then you can consider a single site point ITS. If you can have multiple sites, you can choose between a SWD and a multiple site ITS based on whether or not you observe the roll-out over multiple time points, (SWD) or if you have only one intervention time point (controlled multiple site ITS)

STRATEGIES TO STRENGTHEN EXTERNAL VALIDITY

In a recent article in this journal ( 26 ), the following observation was made that there is an unavoidable trade-off between these two forms of validity such that with a higher control of a study, there is stronger evidence for internal validity but that control may jeopardize some of the external validity of that stronger evidence. Nonetheless, there are design strategies for non-experimental studies that can be undertaken to improve the internal validity while not eliminating considerations of external validity. These are described below across all three study designs.

1. Examine variation of acceptability and reach among diverse sub-populations

One of the strengths of QEDs is that they are often employed to examine intervention effects in real world settings and often, for more diverse populations and settings. Consequently, if there is adequate examination of characteristics of participants and setting-related factors it can be possible to interpret findings among critical groups for which there may be no existing evidence of an intervention effect for. For example in the Campus Watch intervention ( 16 ), the investigator over-sampled the Maori indigenous population in order to be able to stratify the results and investigate whether the program was effective for this under-studied group. In the study by Zombré et al ( 52 ) on health care access in Burkina Faso, the authors examined clinic density characteristics to determine its impact on sustainability.

2. Characterize fidelity and measures of implementation processes

Some of the most important outcomes for examination in these QED studies include whether the intervention was delivered as intended (i.e., fidelity), maintained over the entire study period (i.e., sustainability), and if the outcomes could be specifically examined by this level of fidelity within or across sites. As well, when a complex intervention is related to a policy or guideline shift and implementation requires logistical adjustments (such as phased roll-outs to embed the intervention or to train staff), QEDs more truly mimic real world constraints. As a result, capturing processes of implementation are critical as they can describe important variation in uptake, informing interpretation of the findings for external validity. As described by Prost et al ( 41 ), for example, it is essential to capture what occurs during such phased intervention roll-outs, as with following established guidelines for the development of complex interventions including efforts to define and protocolize activities before their implementation ( 17 , 18 , 28 ). However, QEDs are often conducted by teams with strong interests in adapting the intervention or ‘learning by doing’, which can limit interpretation of findings if not planned into the design. As done in the study by Bailet et al ( 3 ), the investigators refined intervention, based on year 1 data, and then applied in years 2–3, at this later time collecting additional data on training and measurement fidelity. This phasing aspect of implementation generates a tension between protocolizing interventions and adapting them as they go along. When this is the case, additional designs for the intervention roll-out, such as adaptive or hybrid designs can also be considered.

3. Conduct community or cohort-based sampling to improve inference

External validity can be improved when the intervention is applied to entire communities, as with some of the community-randomized studies described in Table 2 ( 12 , 21 ). In these cases, the results are closer to the conditions that would apply if the interventions were conducted ‘at scale’, with a large proportion of a population receiving the intervention. In some cases QEDs also afford greater access for some intervention research to be conducted in remote or difficult to reach communities, where the cost and logistical requirements of an RCT may become prohibitive or may require alteration of the intervention or staffing support to levels that would never be feasible in real world application.

4. Employ a model or framework that covers both internal and external validity

Frameworks can be helpful to enhances interpretability of many kinds of studies, including QEDs and can help ensure that information on essential implementation strategies are included in the results ( 44 ). Although several of the case studies summarized in this article included measures that can improve external validity (such as sub-group analysis of which participants were most impacted, process and contextual measures that can affect variation in uptake), none formally employ an implementation framework. Green and Glasgow (2006) ( 25 ) have outlined several useful criteria for gaging the extent to which an evaluation study also provides measures that enhance interpretation of external validity, for which those employing QEDs could identify relevant components and frameworks to include in reported findings.

It has been observed that it is more difficult to conduct a good quasi-experiment than to conduct a good randomized trial ( 43 ). Although QEDs are increasingly used, it is important to note that randomized designs are still preferred over quasi-experiments except where randomization is not possible. In this paper we present three important QEDs and variants nested within them that can increase internal validity while also improving external validity considerations, and present case studies employing these techniques.

1 It is important to note that if such randomization would be possible at the site level based on similar sites, a cluster randomized control trial would be an option.

LITERATURE CITED