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Quasi Experimental Design Overview & Examples

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What is a Quasi Experimental Design?

A quasi experimental design is a method for identifying causal relationships that does not randomly assign participants to the experimental groups. Instead, researchers use a non-random process. For example, they might use an eligibility cutoff score or preexisting groups to determine who receives the treatment.

Quasi-experimental research is a design that closely resembles experimental research but is different. The term “quasi” means “resembling,” so you can think of it as a cousin to actual experiments. In these studies, researchers can manipulate an independent variable — that is, they change one factor to see what effect it has. However, unlike true experimental research, participants are not randomly assigned to different groups.

Learn more about Experimental Designs: Definition & Types .

When to Use Quasi-Experimental Design

Researchers typically use a quasi-experimental design because they can’t randomize due to practical or ethical concerns. For example:

• Practical Constraints : A school interested in testing a new teaching method can only implement it in preexisting classes and cannot randomly assign students.
• Ethical Concerns : A medical study might not be able to randomly assign participants to a treatment group for an experimental medication when they are already taking a proven drug.

Quasi-experimental designs also come in handy when researchers want to study the effects of naturally occurring events, like policy changes or environmental shifts, where they can’t control who is exposed to the treatment.

Quasi-experimental designs occupy a unique position in the spectrum of research methodologies, sitting between observational studies and true experiments. This middle ground offers a blend of both worlds, addressing some limitations of purely observational studies while navigating the constraints often accompanying true experiments.

A significant advantage of quasi-experimental research over purely observational studies and correlational research is that it addresses the issue of directionality, determining which variable is the cause and which is the effect. In quasi-experiments, an intervention typically occurs during the investigation, and the researchers record outcomes before and after it, increasing the confidence that it causes the observed changes.

However, it’s crucial to recognize its limitations as well. Controlling confounding variables is a larger concern for a quasi-experimental design than a true experiment because it lacks random assignment.

In sum, quasi-experimental designs offer a valuable research approach when random assignment is not feasible, providing a more structured and controlled framework than observational studies while acknowledging and attempting to address potential confounders.

Types of Quasi-Experimental Designs and Examples

Quasi-experimental studies use various methods, depending on the scenario.

Natural Experiments

This design uses naturally occurring events or changes to create the treatment and control groups. Researchers compare outcomes between those whom the event affected and those it did not affect. Analysts use statistical controls to account for confounders that the researchers must also measure.

Natural experiments are related to observational studies, but they allow for a clearer causality inference because the external event or policy change provides both a form of quasi-random group assignment and a definite start date for the intervention.

For example, in a natural experiment utilizing a quasi-experimental design, researchers study the impact of a significant economic policy change on small business growth. The policy is implemented in one state but not in neighboring states. This scenario creates an unplanned experimental setup, where the state with the new policy serves as the treatment group, and the neighboring states act as the control group.

Researchers are primarily interested in small business growth rates but need to record various confounders that can impact growth rates. Hence, they record state economic indicators, investment levels, and employment figures. By recording these metrics across the states, they can include them in the model as covariates and control them statistically. This method allows researchers to estimate differences in small business growth due to the policy itself, separate from the various confounders.

Nonequivalent Groups Design

This method involves matching existing groups that are similar but not identical. Researchers attempt to find groups that are as equivalent as possible, particularly for factors likely to affect the outcome.

For instance, researchers use a nonequivalent groups quasi-experimental design to evaluate the effectiveness of a new teaching method in improving students’ mathematics performance. A school district considering the teaching method is planning the study. Students are already divided into schools, preventing random assignment.

The researchers matched two schools with similar demographics, baseline academic performance, and resources. The school using the traditional methodology is the control, while the other uses the new approach. Researchers are evaluating differences in educational outcomes between the two methods.

They perform a pretest to identify differences between the schools that might affect the outcome and include them as covariates to control for confounding. They also record outcomes before and after the intervention to have a larger context for the changes they observe.

Regression Discontinuity

This process assigns subjects to a treatment or control group based on a predetermined cutoff point (e.g., a test score). The analysis primarily focuses on participants near the cutoff point, as they are likely similar except for the treatment received. By comparing participants just above and below the cutoff, the design controls for confounders that vary smoothly around the cutoff.

For example, in a regression discontinuity quasi-experimental design focusing on a new medical treatment for depression, researchers use depression scores as the cutoff point. Individuals with depression scores just above a certain threshold are assigned to receive the latest treatment, while those just below the threshold do not receive it. This method creates two closely matched groups: one that barely qualifies for treatment and one that barely misses out.

By comparing the mental health outcomes of these two groups over time, researchers can assess the effectiveness of the new treatment. The assumption is that the only significant difference between the groups is whether they received the treatment, thereby isolating its impact on depression outcomes.

Controlling Confounders in a Quasi-Experimental Design

Accounting for confounding variables is a challenging but essential task for a quasi-experimental design.

In a true experiment, the random assignment process equalizes confounders across the groups to nullify their overall effect. It’s the gold standard because it works on all confounders, known and unknown.

Unfortunately, the lack of random assignment can allow differences between the groups to exist before the intervention. These confounding factors might ultimately explain the results rather than the intervention.

Consequently, researchers must use other methods to equalize the groups roughly using matching and cutoff values or statistically adjust for preexisting differences they measure to reduce the impact of confounders.

A key strength of quasi-experiments is their frequent use of “pre-post testing.” This approach involves conducting initial tests before collecting data to check for preexisting differences between groups that could impact the study’s outcome. By identifying these variables early on and including them as covariates, researchers can more effectively control potential confounders in their statistical analysis.

Additionally, researchers frequently track outcomes before and after the intervention to better understand the context for changes they observe.

Statisticians consider these methods to be less effective than randomization. Hence, quasi-experiments fall somewhere in the middle when it comes to internal validity , or how well the study can identify causal relationships versus mere correlation . They’re more conclusive than correlational studies but not as solid as true experiments.

In conclusion, quasi-experimental designs offer researchers a versatile and practical approach when random assignment is not feasible. This methodology bridges the gap between controlled experiments and observational studies, providing a valuable tool for investigating cause-and-effect relationships in real-world settings. Researchers can address ethical and logistical constraints by understanding and leveraging the different types of quasi-experimental designs while still obtaining insightful and meaningful results.

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

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Home » Quasi-Experimental Research Design – Types, Methods

Quasi-Experimental Research Design – Types, Methods

Table of Contents

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.

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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.

Research Methodologies Guide

• Action Research
• Bibliometrics
• Case Studies
• Content Analysis
• Digital Scholarship This link opens in a new window
• Documentary
• Ethnography
• Focus Groups
• Grounded Theory
• Life Histories/Autobiographies
• Longitudinal
• Participant Observation
• Qualitative Research (General)

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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• > The Cambridge Handbook of Research Methods and Statistics for the Social and Behavioral Sciences
• > Quasi-Experimental Research

Book contents

• The Cambridge Handbook of Research Methods and Statistics for the Social and Behavioral Sciences
• Cambridge Handbooks in Psychology
• Copyright page
• Contributors
• Part I From Idea to Reality: The Basics of Research
• Part II The Building Blocks of a Study
• Part III Data Collection
• 13 Cross-Sectional Studies
• 14 Quasi-Experimental Research
• 15 Non-equivalent Control Group Pretest–Posttest Design in Social and Behavioral Research
• 16 Experimental Methods
• 17 Longitudinal Research: A World to Explore
• 18 Online Research Methods
• 19 Archival Data
• 20 Qualitative Research Design
• Part IV Statistical Approaches
• Part V Tips for a Successful Research Career

14 - Quasi-Experimental Research

from Part III - Data Collection

Published online by Cambridge University Press:  25 May 2023

In this chapter, we discuss the logic and practice of quasi-experimentation. Specifically, we describe four quasi-experimental designs – one-group pretest–posttest designs, non-equivalent group designs, regression discontinuity designs, and interrupted time-series designs – and their statistical analyses in detail. Both simple quasi-experimental designs and embellishments of these simple designs are presented. Potential threats to internal validity are illustrated along with means of addressing their potentially biasing effects so that these effects can be minimized. In contrast to quasi-experiments, randomized experiments are often thought to be the gold standard when estimating the effects of treatment interventions. However, circumstances frequently arise where quasi-experiments can usefully supplement randomized experiments or when quasi-experiments can fruitfully be used in place of randomized experiments. Researchers need to appreciate the relative strengths and weaknesses of the various quasi-experiments so they can choose among pre-specified designs or craft their own unique quasi-experiments.

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• Quasi-Experimental Research
• By Charles S. Reichardt , Daniel Storage , Damon Abraham
• Edited by Austin Lee Nichols , Central European University, Vienna , John Edlund , Rochester Institute of Technology, New York
• Book: The Cambridge Handbook of Research Methods and Statistics for the Social and Behavioral Sciences
• Online publication: 25 May 2023
• Chapter DOI: https://doi.org/10.1017/9781009010054.015

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Experimental vs Quasi-Experimental Design: Which to Choose?

Here’s a table that summarizes the similarities and differences between an experimental and a quasi-experimental study design:

What is a quasi-experimental design?

A quasi-experimental design is a non-randomized study design used to evaluate the effect of an intervention. The intervention can be a training program, a policy change or a medical treatment.

Unlike a true experiment, in a quasi-experimental study the choice of who gets the intervention and who doesn’t is not randomized. Instead, the intervention can be assigned to participants according to their choosing or that of the researcher, or by using any method other than randomness.

Having a control group is not required, but if present, it provides a higher level of evidence for the relationship between the intervention and the outcome.

(for more information, I recommend my other article: Understand Quasi-Experimental Design Through an Example ) .

Examples of quasi-experimental designs include:

• One-Group Posttest Only Design
• Static-Group Comparison Design
• One-Group Pretest-Posttest Design
• Separate-Sample Pretest-Posttest Design

What is an experimental design?

An experimental design is a randomized study design used to evaluate the effect of an intervention. In its simplest form, the participants will be randomly divided into 2 groups:

• A treatment group: where participants receive the new intervention which effect we want to study.
• A control or comparison group: where participants do not receive any intervention at all (or receive some standard intervention).

Randomization ensures that each participant has the same chance of receiving the intervention. Its objective is to equalize the 2 groups, and therefore, any observed difference in the study outcome afterwards will only be attributed to the intervention – i.e. it removes confounding.

(for more information, I recommend my other article: Purpose and Limitations of Random Assignment ).

Examples of experimental designs include:

• Posttest-Only Control Group Design
• Pretest-Posttest Control Group Design
• Solomon Four-Group Design
• Matched Pairs Design
• Randomized Block Design

When to choose an experimental design over a quasi-experimental design?

Although many statistical techniques can be used to deal with confounding in a quasi-experimental study, in practice, randomization is still the best tool we have to study causal relationships.

Another problem with quasi-experiments is the natural progression of the disease or the condition under study — When studying the effect of an intervention over time, one should consider natural changes because these can be mistaken with changes in outcome that are caused by the intervention. Having a well-chosen control group helps dealing with this issue.

So, if losing the element of randomness seems like an unwise step down in the hierarchy of evidence, why would we ever want to do it?

This is what we’re going to discuss next.

When to choose a quasi-experimental design over a true experiment?

The issue with randomness is that it cannot be always achievable.

So here are some cases where using a quasi-experimental design makes more sense than using an experimental one:

• If being in one group is believed to be harmful for the participants , either because the intervention is harmful (ex. randomizing people to smoking), or the intervention has a questionable efficacy, or on the contrary it is believed to be so beneficial that it would be malevolent to put people in the control group (ex. randomizing people to receiving an operation).
• In cases where interventions act on a group of people in a given location , it becomes difficult to adequately randomize subjects (ex. an intervention that reduces pollution in a given area).
• When working with small sample sizes , as randomized controlled trials require a large sample size to account for heterogeneity among subjects (i.e. to evenly distribute confounding variables between the intervention and control groups).

Further reading

• Statistical Software Popularity in 40,582 Research Papers
• Checking the Popularity of 125 Statistical Tests and Models
• Objectives of Epidemiology (With Examples)
• 12 Famous Epidemiologists and Why

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• Quasi-Experimental Design | Definition, Types & Examples

Quasi-Experimental Design | Definition, Types & Examples

Published on 11 April 2022 by Lauren Thomas . Revised on 22 January 2024.

Like a true experiment , a quasi-experimental design aims to establish a cause-and-effect relationship between an independent and dependent variable .

However, unlike a true experiment, a quasi-experiment does not rely on random assignment . Instead, subjects are assigned to groups based on non-random criteria.

Quasi-experimental design is a useful tool in situations where true experiments cannot be used for ethical or practical reasons.

Table of contents

Differences between quasi-experiments and true experiments, types of quasi-experimental designs, when to use quasi-experimental design, advantages and disadvantages, frequently asked questions about quasi-experimental design.

There are several common differences between true and quasi-experimental designs.

Example of a true experiment vs a quasi-experiment

However, for ethical reasons, the directors of the mental health clinic may not give you permission to randomly assign their patients to treatments. In this case, you cannot run a true experiment.

Instead, you can use a quasi-experimental design.

You can use these pre-existing groups to study the symptom progression of the patients treated with the new therapy versus those receiving the standard course of treatment.

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Many types of quasi-experimental designs exist. Here we explain three of the most common types: nonequivalent groups design, regression discontinuity, and natural experiments.

Nonequivalent groups design

In nonequivalent group design, the researcher chooses existing groups that appear similar, but where only one of the groups experiences the treatment.

In a true experiment with random assignment , the control and treatment groups are considered equivalent in every way other than the treatment. But in a quasi-experiment where the groups are not random, they may differ in other ways – they are nonequivalent groups .

When using this kind of design, researchers try to account for any confounding variables by controlling for them in their analysis or by choosing groups that are as similar as possible.

This is the most common type of quasi-experimental design.

Regression discontinuity

Many potential treatments that researchers wish to study are designed around an essentially arbitrary cutoff, where those above the threshold receive the treatment and those below it do not.

Near this threshold, the differences between the two groups are often so minimal as to be nearly nonexistent. Therefore, researchers can use individuals just below the threshold as a control group and those just above as a treatment group.

However, since the exact cutoff score is arbitrary, the students near the threshold – those who just barely pass the exam and those who fail by a very small margin – tend to be very similar, with the small differences in their scores mostly due to random chance. You can therefore conclude that any outcome differences must come from the school they attended.

Natural experiments

In both laboratory and field experiments, researchers normally control which group the subjects are assigned to. In a natural experiment, an external event or situation (‘nature’) results in the random or random-like assignment of subjects to the treatment group.

Even though some use random assignments, natural experiments are not considered to be true experiments because they are observational in nature.

Although the researchers have no control over the independent variable, they can exploit this event after the fact to study the effect of the treatment.

However, as they could not afford to cover everyone who they deemed eligible for the program, they instead allocated spots in the program based on a random lottery.

Although true experiments have higher internal validity , you might choose to use a quasi-experimental design for ethical or practical reasons.

Sometimes it would be unethical to provide or withhold a treatment on a random basis, so a true experiment is not feasible. In this case, a quasi-experiment can allow you to study the same causal relationship without the ethical issues.

The Oregon Health Study is a good example. It would be unethical to randomly provide some people with health insurance but purposely prevent others from receiving it solely for the purposes of research.

However, since the Oregon government faced financial constraints and decided to provide health insurance via lottery, studying this event after the fact is a much more ethical approach to studying the same problem.

True experimental design may be infeasible to implement or simply too expensive, particularly for researchers without access to large funding streams.

At other times, too much work is involved in recruiting and properly designing an experimental intervention for an adequate number of subjects to justify a true experiment.

In either case, quasi-experimental designs allow you to study the question by taking advantage of data that has previously been paid for or collected by others (often the government).

Quasi-experimental designs have various pros and cons compared to other types of studies.

• Higher external validity than most true experiments, because they often involve real-world interventions instead of artificial laboratory settings.
• Higher internal validity than other non-experimental types of research, because they allow you to better control for confounding variables than other types of studies do.
• Lower internal validity than true experiments – without randomisation, it can be difficult to verify that all confounding variables have been accounted for.
• The use of retrospective data that has already been collected for other purposes can be inaccurate, incomplete or difficult to access.

A quasi-experiment is a type of research design that attempts to establish a cause-and-effect relationship. The main difference between this and a true experiment is that the groups are not randomly assigned.

In experimental research, random assignment is a way of placing participants from your sample into different groups using randomisation. With this method, every member of the sample has a known or equal chance of being placed in a control group or an experimental group.

Quasi-experimental design is most useful in situations where it would be unethical or impractical to run a true experiment .

Quasi-experiments have lower internal validity than true experiments, but they often have higher external validity  as they can use real-world interventions instead of artificial laboratory settings.

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Explaining Quasi-Experimental Design And Its Various Methods

• September 27, 2021

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 As you strive to uncover causal (cause-and-effect) relationships between variables, you may often encounter ethical or practical constraints while conducting controlled experiments. 

Quasi-experimental design steps in as a powerful alternative that helps you overcome these challenges and offer valuable insights. 

In this blog, we’ll look into its characteristics, examples, types, and how it differs from true-experimental research design. The purpose of this blog is to understand how this research methodology bridges the gap between a fully controlled experiment and a purely observational study.

What Is Quasi-Experimental Design?

A quasi-experimental design is pretty much different from an experimental design, except for the fact that they both manifest the cause-effect relationship between the independent and dependent variables . 

So, how is quasi-experimental design different? 

Well, unlike experimental design, quasi-experiments do not include random assignments of participants meaning, the participants are placed in the experimental groups based on some of the other criteria. Let us take a deeper look at how quasi-experimental design works.

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Experimental design has three characteristics:, 1. manipulation.

Manipulation simply means evaluating the effect of the independent variable on the dependent variable. 

Example: A chocolate and a crying child.

• Independent variable:  Type of chocolate. 
• Dependent variable: The child is crying for chocolate.

So manipulation means the effect of an independent variable, that is, chocolate, on the dependent variable, that is, the crying child. In short, you are using an outside source on the dependent variable. This proves that after getting the chocolate (independent variable), the child stops crying (dependent variable).

2. Randomization

Randomization means sudden selection without any plan. Example: A lottery system. The lottery numbers are announced at random so everyone who buys a lottery has an equal chance. Hence, it means you select a sample without any plan and everyone has an equal chance of getting into any one of the experimental groups.

This means using a control group in the experiment. In this group, researchers keep the independent variable constant. This control group is then compared to a treatment group, where the researchers have changed the independent variable. Well, for obvious reasons, researchers are more interested in the treatment group as it has a scope of change in the dependent variable. 

Example: You want to find out whether the workers work more efficiently if there is a pay raise. 

Here, you will put certain workers in the treatment group and some in the control group.

• Treatment group: You pay more to the workers
• Control group: You don’t pay any extra to the workers, and things remain the same. 

By comparing these two groups, you understand that the workers who got paid more worked more efficiently than the workers who didn’t. 

As for the quasi-experimental design, the manipulation characteristic of the true experiment remains the same. However randomization or control characteristics are present in contrast to each other or none at all. 

Hence, these experiments are conducted where random selection is difficult or even impossible. The quasi-experiment does not include random assignment, as the independent variable is manipulated before the measurement of the dependent variable.

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What are the types of quasi-experimental design?

Amongst all the various types of quasi-experimental design, let us first get to know two main types of quasi-experimental design:

• Non-equivalent group design (NEGD)
• Regression discontinuity design

1. Non-Equivalent Group Design (NEGD)

You can picture non-equivalent group designs as a mixture of both true experimental design as well as quasi-experimental design. The reason is, that it uses both their qualities. Like a true experiment, NEGD uses the pre-existing groups that we feel are similar, namely treatment and control groups. However it lacks the randomization characteristic of a quasi-experiment. 

While grouping, researchers see to it that they are not influenced by any third variables or confounding variables. Hence, the groups are as similar as possible. For example, when talking about political study, we might select groups that are more similar to each other. 

Let us understand it with an example:

Take the previous example where you studied whether the workers work more efficiently if there is a pay rise. 

You give a pre-test to the workers in one company while their pay is normal. Then you put them under the treatment group where they work and their pay is being increased. After the experiment, you take their post-test about their experience and attitude towards their work. 

Later, you give the same pre-test to the workers from a similar company and put them in a control group where their pay is not raised, and then conduct a post-test. 

Hence, the Non-equivalent design has a name to remind us that the groups are not equivalent and are not assigned on a random practice. 

2. Regression discontinuity design or RDD

Regression discontinuity design, or RDD, is a quasi-experimental design technique that computes the influence of a treatment or intervention. It does so by using a mechanism that assigns the treatment based on eligibility, known as a “cut-off”.

So the participants above the cut-off get to be in a treatment group and those below the cut-off doesn’t. Although the difference between these two groups is negligible. 

Let’s take a look at an example:

A school wants to grant a $50 scholarship to students, depending on an independent test taken to measure their intellect and household. 

Those who pass the test will get a scholarship. However, the students who are just below the cut-off and those just above it can be considered similar. We can say the differences in their scores occurred randomly. Hence you can keep on studying both groups to get a long-term outcome.

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What are the advantages of a quasi-experimental design?

The quasi-experiment design, also known as external validity, can be perfect for determining what is best for the population. Let’s look at some advantages of this research methodology type. 

• It gives the researchers power over the variables by being able to control them.
• The quasi-experiment method can be combined with other experimental methods too.
• It provides transferability to a greater extent.
• It is an intuitive process that is well-shaped by the researchers. 
• Involves real-world problems and solutions and not any artificial ones. 
• Offers better control over the third variable, known as the confounding variable, which influences the cause and effect. 

What are the disadvantages of a quasi-experimental design?

As a research design, it is bound to have some limitations, let’s look at some of the disadvantages you should consider when selecting the design for your research. 

• It serves less internal validity than true experiments.
• Due to no randomization, you cannot tell for sure that the confounding or third variable is eradicated. 
• It has scope for human errors.
• It can allow the researcher’s personal bias to get involved. 
• Human responses are difficult to measure; hence, there is a chance that the results will be produced artificially.
• Using old or backdated data can be incorrect and inadequate for the study.

Other Quasi-Experimental Designs

Apart from the above-mentioned types, there are other equally important quasi-experimental designs that have different applications depending on their characteristics and their respective design notations . 

Let’s take a look at all of them in detail:

1. The proxy Pre-Test Design

The proxy pre-test design works the same as a typical pre-test and post-test design. Except, the pre-test here is conducted AFTER the treatment is given. Got confused? How is it pre-test if it is conducted after? Well, the keyword here is “proxy”. These proxy variables tell where the groups would have been in the pre-test. 

You ask the group after their program about how they’d have answered the same questions before their treatment. Although, this technique is not very reliable as we cannot expect the participants to remember how they felt a long time ago, and we surely cannot tell if they are faking their answers. 

As this design is highly not recommended, you can use this under some unavoidable circumstances like the treatment has already begun and you couldn’t take the pre-test. 

In such cases, this approach will help rather than depending totally on the post-test.

You want to study the workers’ performance after the pay rise. But you were called to do the pre-test after the program had started. In that case, you will have to take the post-test and study a proxy variable, such as productivity from the time before the program and after the program

2. The Separate Pre-Post Samples Design

This technique also works on the pre-test and post-test designs. The difference is that the participants you used for the pre-test won’t be the same for the post-test. 

You want to study the client satisfaction of two similar companies. You take one for the treatment and the other for the control. Let’s say you conducted a pre-test in both companies at the same time and then begin your experiment. 

After a while, when the program is complete, you go to take a post-test. Now, the set of clients you take in for the test is going to be different than the pre-test ones, the reason being clients change after the course of the period. 

In this case, you cannot derive one-to-one results, but you can tell the average client satisfaction in both companies. 

3. The Double Pre-Test Design

The double pre-test design is a very robust quasi-experimental design designed to rule out the internal validity problem we had with the non-equivalent design. It has two pre-tests before the program. It is when the two groups are progressing at a different pace that you should change from pre-test 1 to pre-test 2. 

Due to the benefit of two pre-tests, you can determine the null case scenario. It assumes the difference between the scores in the pre-test and post-test is due to random chance, as it doesn’t allow one person to take the pre-test twice.

4. The Switching Replications Design

In the switching replications design, as the name suggests, the role of the group is switched. It follows the same treatment-control group pattern, except it has two phases.

Phase 1: Both the groups are pre-tested, then they undergo their respective program. Later they are post-tested.

Phase 2: In this phase, an original treatment group is now a control group and an original control group is now a treatment group.

The main benefit of inculcating this design is that it proves strong against internal validation as well as external validation. The reason is that two parallel implementations of the program allow all the participants to experience the program, making it ethically strong as well.

5.The Non-equivalent Dependent Variables (NEDV) Design

NEDV design, in its simplest form, is not the most reliable one and does not work wonders against internal validity either. But then, what is the use of NEDV? 

Well, sometimes the treatment group may be affected by some external factors. Hence, there are two pre and post-tests applied to the participants, one regarding the treatment itself and the other regarding that external variable. 

Wait, how about we take an example to understand this?

Let us say you started a program to test history teaching techniques. You design standards tests for history (treatment group) and show historical movies (external variable). Later in the post-tests, you find out that along with the history scores, students’ interest in historical movies has also increased, suggesting that showing historical movies has influenced students to study the subject.

6. The regression Point Displacement (RPD) Design

RPD design is used when measures for already existing groups are available and can be compared with those for treatment groups. The treatment group is the only group present, and both pre-test and post-tests are conducted. 

This method is widely beneficial for larger groups, communities, and companies. RPD works by comparing a single program unit with a larger comparison unit.

Consider a community-based COVID awareness program. It has been decided to start the initiative in a particular town or a vast district. The representatives forecast the active cases in that town and use the remaining towns as a comparison. Now rather than giving the average for the rest of the towns’ COVID cases, they show their count.

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All that studying but shouldn’t you know when to perfectly use quasi-experiments? Well, now as we are to the end of the matter, let us discuss when to use quasi-experiments and for what reasons. 

1. For ethical reasons

Remember when we discussed the “willingness” of obese people to participate in the experiment? That is when ethics start to matter. You cannot go on putting random participants under treatments as you do with true experiments. 

Especially when it directly affects the participants’ lives. One of the best examples is Oregon Health Study where health insurance is given to certain people while others were restricted from it. 

2. For practical reasons

True experiments, despite having higher internal validity, can be expensive. Also, it requires enough participants so that the true experiment can be justified. Unlike that, in a quasi-experiment, you can use the already gathered data. 

The data is collected and paid by some strong entity, say the government, and you use that to study your questions. 

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Also read: Experimental Research .

Differences between quasi-experiments and true experiments

The above description is overwhelming? Don’t worry. Here is the straight difference between the quasi-experiments and true experiments so that you can understand how both vary from each other.

Example of true-experimental design:

While starting the true experiment, you assign some participants in the treatment group where they are fed only junk food. While the other half of the participants go to the control group , where they have their regular ongoing diet (standard course).

You decide to take obese people’s reports every day after their meals to note down their health and discomfort, if any.

However, participants who are assigned to the treatment group would not like to change their diet to complete junk food for personal reasons. In this case, you cannot conduct a true experiment against their will. This is when quasi-experiment comes in.

Example of quasi-experimental design:

While talking to the participants, you find out that some of the participants want to try the junk food effect while the others don’t want to experiment with their diet and choose to stick with a regular diet.

You can now assign already existing groups to the participants according to their choices. Study how the regular consumption of junk food affects the obese from that group. 

Here, you did not assign groups to the random participants and can be confident about the difference occurring due to the conducted experiment. 

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Quasi-experimental design has a unique approach that allows you to uncover causal relationship between variables when controlled experiments are not feasible or ethical. While it may not posses the level of control and randomization that you have when performing true-experiment; quasi-experimental research design enables you to make meaningful contribution by providing valuable insights to various fields.

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The use and interpretation of quasi-experimental design

Last updated

6 February 2023

Reviewed by

Miroslav Damyanov

Short on time? Get an AI generated summary of this article instead

• What is a quasi-experimental design?

Commonly used in medical informatics (a field that uses digital information to ensure better patient care), researchers generally use this design to evaluate the effectiveness of a treatment – perhaps a type of antibiotic or psychotherapy, or an educational or policy intervention.

Even though quasi-experimental design has been used for some time, relatively little is known about it. Read on to learn the ins and outs of this research design.

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• When to use a quasi-experimental design

A quasi-experimental design is used when it's not logistically feasible or ethical to conduct randomized, controlled trials. As its name suggests, a quasi-experimental design is almost a true experiment. However, researchers don't randomly select elements or participants in this type of research.

Researchers prefer to apply quasi-experimental design when there are ethical or practical concerns. Let's look at these two reasons more closely.

Ethical reasons

In some situations, the use of randomly assigned elements can be unethical. For instance, providing public healthcare to one group and withholding it to another in research is unethical. A quasi-experimental design would examine the relationship between these two groups to avoid physical danger.

Practical reasons

Randomized controlled trials may not be the best approach in research. For instance, it's impractical to trawl through large sample sizes of participants without using a particular attribute to guide your data collection .

Recruiting participants and properly designing a data-collection attribute to make the research a true experiment requires a lot of time and effort, and can be expensive if you don’t have a large funding stream.

A quasi-experimental design allows researchers to take advantage of previously collected data and use it in their study.

• Examples of quasi-experimental designs

Quasi-experimental research design is common in medical research, but any researcher can use it for research that raises practical and ethical concerns. Here are a few examples of quasi-experimental designs used by different researchers:

Example 1: Determining the effectiveness of math apps in supplementing math classes

A school wanted to supplement its math classes with a math app. To select the best app, the school decided to conduct demo tests on two apps before selecting the one they will purchase.

Scope of the research

Since every grade had two math teachers, each teacher used one of the two apps for three months. They then gave the students the same math exams and compared the results to determine which app was most effective.

Reasons why this is a quasi-experimental study

This simple study is a quasi-experiment since the school didn't randomly assign its students to the applications. They used a pre-existing class structure to conduct the study since it was impractical to randomly assign the students to each app.

Example 2: Determining the effectiveness of teaching modern leadership techniques in start-up businesses

A hypothetical quasi-experimental study was conducted in an economically developing country in a mid-sized city.

Five start-ups in the textile industry and five in the tech industry participated in the study. The leaders attended a six-week workshop on leadership style, team management, and employee motivation.

After a year, the researchers assessed the performance of each start-up company to determine growth. The results indicated that the tech start-ups were further along in their growth than the textile companies.

The basis of quasi-experimental research is a non-randomized subject-selection process. This study didn't use specific aspects to determine which start-up companies should participate. Therefore, the results may seem straightforward, but several aspects may determine the growth of a specific company, apart from the variables used by the researchers.

Example 3: A study to determine the effects of policy reforms and of luring foreign investment on small businesses in two mid-size cities

In a study to determine the economic impact of government reforms in an economically developing country, the government decided to test whether creating reforms directed at small businesses or luring foreign investments would spur the most economic development.

The government selected two cities with similar population demographics and sizes. In one of the cities, they implemented specific policies that would directly impact small businesses, and in the other, they implemented policies to attract foreign investment.

After five years, they collected end-of-year economic growth data from both cities. They looked at elements like local GDP growth, unemployment rates, and housing sales.

The study used a non-randomized selection process to determine which city would participate in the research. Researchers left out certain variables that would play a crucial role in determining the growth of each city. They used pre-existing groups of people based on research conducted in each city, rather than random groups.

• Advantages of a quasi-experimental design

Some advantages of quasi-experimental designs are:

Researchers can manipulate variables to help them meet their study objectives.

It offers high external validity, making it suitable for real-world applications, specifically in social science experiments.

Integrating this methodology into other research designs is easier, especially in true experimental research. This cuts down on the time needed to determine your outcomes.

• Disadvantages of a quasi-experimental design

Despite the pros that come with a quasi-experimental design, there are several disadvantages associated with it, including the following:

It has a lower internal validity since researchers do not have full control over the comparison and intervention groups or between time periods because of differences in characteristics in people, places, or time involved. It may be challenging to determine whether all variables have been used or whether those used in the research impacted the results.

There is the risk of inaccurate data since the research design borrows information from other studies.

There is the possibility of bias since researchers select baseline elements and eligibility.

• What are the different quasi-experimental study designs?

There are three distinct types of quasi-experimental designs:

Nonequivalent

Regression discontinuity, natural experiment.

This is a hybrid of experimental and quasi-experimental methods and is used to leverage the best qualities of the two. Like the true experiment design, nonequivalent group design uses pre-existing groups believed to be comparable. However, it doesn't use randomization, the lack of which is a crucial element for quasi-experimental design.

Researchers usually ensure that no confounding variables impact them throughout the grouping process. This makes the groupings more comparable.

Example of a nonequivalent group design

A small study was conducted to determine whether after-school programs result in better grades. Researchers randomly selected two groups of students: one to implement the new program, the other not to. They then compared the results of the two groups.

This type of quasi-experimental research design calculates the impact of a specific treatment or intervention. It uses a criterion known as "cutoff" that assigns treatment according to eligibility.

Researchers often assign participants above the cutoff to the treatment group. This puts a negligible distinction between the two groups (treatment group and control group).

Example of regression discontinuity

Students must achieve a minimum score to be enrolled in specific US high schools. Since the cutoff score used to determine eligibility for enrollment is arbitrary, researchers can assume that the disparity between students who only just fail to achieve the cutoff point and those who barely pass is a small margin and is due to the difference in the schools that these students attend.

Researchers can then examine the long-term effects of these two groups of kids to determine the effect of attending certain schools. This information can be applied to increase the chances of students being enrolled in these high schools.

This research design is common in laboratory and field experiments where researchers control target subjects by assigning them to different groups. Researchers randomly assign subjects to a treatment group using nature or an external event or situation.

However, even with random assignment, this research design cannot be called a true experiment since nature aspects are observational. Researchers can also exploit these aspects despite having no control over the independent variables.

Example of the natural experiment approach

An example of a natural experiment is the 2008 Oregon Health Study.

Oregon intended to allow more low-income people to participate in Medicaid.

Since they couldn't afford to cover every person who qualified for the program, the state used a random lottery to allocate program slots.

Researchers assessed the program's effectiveness by assigning the selected subjects to a randomly assigned treatment group, while those that didn't win the lottery were considered the control group.

• Differences between quasi-experiments and true experiments

There are several differences between a quasi-experiment and a true experiment:

Participants in true experiments are randomly assigned to the treatment or control group, while participants in a quasi-experiment are not assigned randomly.

In a quasi-experimental design, the control and treatment groups differ in unknown or unknowable ways, apart from the experimental treatments that are carried out. Therefore, the researcher should try as much as possible to control these differences.

Quasi-experimental designs have several "competing hypotheses," which compete with experimental manipulation to explain the observed results.

Quasi-experiments tend to have lower internal validity (the degree of confidence in the research outcomes) than true experiments, but they may offer higher external validity (whether findings can be extended to other contexts) as they involve real-world interventions instead of controlled interventions in artificial laboratory settings.

Despite the distinct difference between true and quasi-experimental research designs, these two research methodologies share the following aspects:

Both study methods subject participants to some form of treatment or conditions.

Researchers have the freedom to measure some of the outcomes of interest.

Researchers can test whether the differences in the outcomes are associated with the treatment.

• An example comparing a true experiment and quasi-experiment

Imagine you wanted to study the effects of junk food on obese people. Here's how you would do this as a true experiment and a quasi-experiment:

How to carry out a true experiment

In a true experiment, some participants would eat junk foods, while the rest would be in the control group, adhering to a regular diet. At the end of the study, you would record the health and discomfort of each group.

This kind of experiment would raise ethical concerns since the participants assigned to the treatment group are required to eat junk food against their will throughout the experiment. This calls for a quasi-experimental design.

How to carry out a quasi-experiment

In quasi-experimental research, you would start by finding out which participants want to try junk food and which prefer to stick to a regular diet. This allows you to assign these two groups based on subject choice.

In this case, you didn't assign participants to a particular group, so you can confidently use the results from the study.

When is a quasi-experimental design used?

Quasi-experimental designs are used when researchers don’t want to use randomization when evaluating their intervention.

What are the characteristics of quasi-experimental designs?

Some of the characteristics of a quasi-experimental design are:

Researchers don't randomly assign participants into groups, but study their existing characteristics and assign them accordingly.

Researchers study the participants in pre- and post-testing to determine the progress of the groups.

Quasi-experimental design is ethical since it doesn’t involve offering or withholding treatment at random.

Quasi-experimental design encompasses a broad range of non-randomized intervention studies. This design is employed when it is not ethical or logistically feasible to conduct randomized controlled trials. Researchers typically employ it when evaluating policy or educational interventions, or in medical or therapy scenarios.

How do you analyze data in a quasi-experimental design?

You can use two-group tests, time-series analysis, and regression analysis to analyze data in a quasi-experiment design. Each option has specific assumptions, strengths, limitations, and data requirements.

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Chapter 7: Nonexperimental Research

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). [1] 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 design 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) [2] . 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) [3] . 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 parallel 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: Classics in the History of Psychology .

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) [4] . 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.

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 one 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) [5] . 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 7.3 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 7.3 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 7.3 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.

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 change in attitude 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 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.
• regression to the mean
• spontaneous remission

Image Descriptions

Figure 7.3 image description: Two line graphs charting the number of absences per week over 14 weeks. The first 7 weeks are without treatment and the last 7 weeks are with treatment. In the first line graph, there are between 4 to 8 absences each week. After the treatment, the absences drop to 0 to 3 each week, which suggests the treatment worked. In the second line graph, there is no noticeable change in the number of absences per week after the treatment, which suggests the treatment did not work. [Return to Figure 7.3]

• Cook, T. D., & Campbell, D. T. (1979). Quasi-experimentation: Design & analysis issues in field settings . Boston, MA: Houghton Mifflin. ↵
• 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. ↵
• Eysenck, H. J. (1952). The effects of psychotherapy: An evaluation. Journal of Consulting Psychology, 16 , 319–324. ↵
• Smith, M. L., Glass, G. V., & Miller, T. I. (1980). The benefits of psychotherapy . Baltimore, MD: Johns Hopkins University Press. ↵

A between-subjects design in which participants have not been randomly assigned to conditions.

The dependent variable is measured once before the treatment is implemented and once after it is implemented.

A category of alternative explanations for differences between scores such as events that happened between the pretest and posttest, unrelated to the study.

An alternative explanation that refers to how the participants might have changed between the pretest and posttest in ways that they were going to anyway because they are growing and learning.

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.

The tendency for many medical and psychological problems to improve over time without any form of treatment.

A set of measurements taken at intervals over a period of time that are interrupted by a treatment.

Research Methods in Psychology - 2nd Canadian Edition Copyright © 2015 by Paul C. Price, Rajiv Jhangiani, & I-Chant A. Chiang is licensed under a Creative Commons Attribution-NonCommercial-ShareAlike 4.0 International License , except where otherwise noted.

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5 Chapter 5: Experimental and Quasi-Experimental Designs

Case stu dy: the impact of teen court.

Research Study

An Experimental Evaluation of Teen Courts 1

Research Question

Is teen court more effective at reducing recidivism and improving attitudes than traditional juvenile justice processing?

Methodology

Researchers randomly assigned 168 juvenile offenders ages 11 to 17 from four different counties in Maryland to either teen court as experimental group members or to traditional juvenile justice processing as control group members. (Note: Discussion on the technical aspects of experimental designs, including random assignment, is found in detail later in this chapter.) Of the 168 offenders, 83 were assigned to teen court and 85 were assigned to regular juvenile justice processing through random assignment. Of the 83 offenders assigned to the teen court experimental group, only 56 (67%) agreed to participate in the study. Of the 85 youth randomly assigned to normal juvenile justice processing, only 51 (60%) agreed to participate in the study.

Upon assignment to teen court or regular juvenile justice processing, all offenders entered their respective sanction. Approximately four months later, offenders in both the experimental group (teen court) and the control group (regular juvenile justice processing) were asked to complete a post-test survey inquiring about a variety of behaviors (frequency of drug use, delinquent behavior, variety of drug use) and attitudinal measures (social skills, rebelliousness, neighborhood attachment, belief in conventional rules, and positive self-concept). The study researchers also collected official re-arrest data for 18 months starting at the time of offender referral to juvenile justice authorities.

Teen court participants self-reported higher levels of delinquency than those processed through regular juvenile justice processing. According to official re-arrests, teen court youth were re-arrested at a higher rate and incurred a higher average number of total arrests than the control group. Teen court offenders also reported significantly lower scores on survey items designed to measure their �belief in conventional rules� compared to offenders processed through regular juvenile justice avenues. Other attitudinal and opinion measures did not differ significantly between the experimental and control group members based on their post-test responses. In sum, those youth randomly assigned to teen court fared worse than control group members who were not randomly assigned to teen court.

Limitations with the Study Procedure

Limitations are inherent in any research study and those research efforts that utilize experimental designs are no exception. It is important to consider the potential impact that a limitation of the study procedure could have on the results of the study.

In the current study, one potential limitation is that teen courts from four different counties in Maryland were utilized. Because of the diversity in teen court sites, it is possible that there were differences in procedure between the four teen courts and such differences could have impacted the outcomes of this study. For example, perhaps staff members at one teen court were more punishment-oriented than staff members at the other county teen courts. This philosophical difference may have affected treatment delivery and hence experimental group members� belief in conventional attitudes and recidivism. Although the researchers monitored each teen court to help ensure treatment consistency between study sites, it is possible that differences existed in the day-to-day operation of the teen courts that may have affected participant outcomes. This same limitation might also apply to control group members who were sanctioned with regular juvenile justice processing in four different counties.

A researcher must also consider the potential for differences between the experimental and control group members. Although the offenders were randomly assigned to the experimental or control group, and the assumption is that the groups were equivalent to each other prior to program participation, the researchers in this study were only able to compare the experimental and control groups on four variables: age, school grade, gender, and race. It is possible that the experimental and control group members differed by chance on one or more factors not measured or available to the researchers. For example, perhaps a large number of teen court members experienced problems at home that can explain their more dismal post-test results compared to control group members without such problems. A larger sample of juvenile offenders would likely have helped to minimize any differences between the experimental and control group members. The collection of additional information from study participants would have also allowed researchers to be more confident that the experimental and control group members were equivalent on key pieces of information that could have influenced recidivism and participant attitudes.

Finally, while 168 juvenile offenders were randomly assigned to either the experimental or control group, not all offenders agreed to participate in the evaluation. Remember that of the 83 offenders assigned to the teen court experimental group, only 56 (67%) agreed to participate in the study. Of the 85 youth randomly assigned to normal juvenile justice processing, only 51 (60%) agreed to participate in the study. While this limitation is unavoidable, it still could have influenced the study. Perhaps those 27 offenders who declined to participate in the teen court group differed significantly from the 56 who agreed to participate. If so, it is possible that the differences among those two groups could have impacted the results of the study. For example, perhaps the 27 youths who were randomly assigned to teen court but did not agree to be a part of the study were some of the least risky of potential teen court participants�less serious histories, better attitudes to begin with, and so on. In this case, perhaps the most risky teen court participants agreed to be a part of the study, and as a result of being more risky, this led to more dismal delinquency outcomes compared to the control group at the end of each respective program. Because parental consent was required for the study authors to be able to compare those who declined to participate in the study to those who agreed, it is unknown if the participants and nonparticipants differed significantly on any variables among either the experimental or control group. Moreover, of the resulting 107 offenders who took part in the study, only 75 offenders accurately completed the post-test survey measuring offending and attitudinal outcomes.

Again, despite the experimental nature of this study, such limitations could have impacted the study results and must be considered.

Impact on Criminal Justice

Teen courts are generally designed to deal with nonserious first time offenders before they escalate to more serious and chronic delinquency. Innovative programs such as �Scared Straight� and juvenile boot camps have inspired an increase in teen court programs across the country, although there is little evidence regarding their effectiveness compared to traditional sanctions for youthful offenders. This study provides more specific evidence as to the effectiveness of teen courts relative to normal juvenile justice processing. Researchers learned that teen court participants fared worse than those in the control group. The potential labeling effects of teen court, including stigma among peers, especially where the offense may have been very minor, may be more harmful than doing less or nothing. The real impact of this study lies in the recognition that teen courts and similar sanctions for minor offenders may do more harm than good.

One important impact of this study is that it utilized an experimental design to evaluate the effectiveness of a teen court compared to traditional juvenile justice processing. Despite the study�s limitations, by using an experimental design it improved upon previous teen court evaluations by attempting to ensure any results were in fact due to the treatment, not some difference between the experimental and control group. This study also utilized both official and self-report measures of delinquency, in addition to self-report measures on such factors as self-concept and belief in conventional rules, which have been generally absent from teen court evaluations. The study authors also attempted to gauge the comparability of the experimental and control groups on factors such as age, gender, and race to help make sure study outcomes were attributable to the program, not the participants.

In This Chapter You Will Learn

The four components of experimental and quasi-experimental research designs and their function in answering a research question

The differences between experimental and quasi-experimental designs

The importance of randomization in an experimental design

The types of questions that can be answered with an experimental or quasi-experimental research design

About the three factors required for a causal relationship

That a relationship between two or more variables may appear causal, but may in fact be spurious, or explained by another factor

That experimental designs are relatively rare in criminal justice and why

About common threats to internal validity or alternative explanations to what may appear to be a causal relationship between variables

Why experimental designs are superior to quasi-experimental designs for eliminating or reducing the potential of alternative explanations

Introduction

The teen court evaluation that began this chapter is an example of an experimental design. The researchers of the study wanted to determine whether teen court was more effective at reducing recidivism and improving attitudes compared to regular juvenile justice case processing. In short, the researchers were interested in the relationship between variables �the relationship of teen court to future delinquency and other outcomes. When researchers are interested in whether a program, policy, practice, treatment, or other intervention impacts some outcome, they often utilize a specific type of research method/design called experimental design. Although there are many types of experimental designs, the foundation for all of them is the classic experimental design. This research design, and some typical variations of this experimental design, are the focus of this chapter.

Although the classic experiment may be appropriate to answer a particular research question, there are barriers that may prevent researchers from using this or another type of experimental design. In these situations, researchers may turn to quasi-experimental designs. Quasi-experiments include a group of research designs that are missing a key element found in the classic experiment and other experimental designs (hence the term �quasi� experiment). Despite this missing part, quasi-experiments are similar in structure to experimental designs and are used to answer similar types of research questions. This chapter will also focus on quasi-experiments and how they are similar to and different from experimental designs.

Uncovering the relationship between variables, such as the impact of teen court on future delinquency, is important in criminal justice and criminology, just as it is in other scientific disciplines such as education, biology, and medicine. Indeed, whereas criminal justice researchers may be interested in whether a teen court reduces recidivism or improves attitudes, medical field researchers may be concerned with whether a new drug reduces cholesterol, or an education researcher may be focused on whether a new teaching style leads to greater academic gains. Across these disciplines and topics of interest, the experimental design is appropriate. In fact, experimental designs are used in all scientific disciplines; the only thing that changes is the topic. Specific to criminal justice, below is a brief sampling of the types of questions that can be addressed using an experimental design:

Does participation in a correctional boot camp reduce recidivism?

What is the impact of an in-cell integration policy on inmate-on-inmate assaults in prisons?

Does police officer presence in schools reduce bullying?

Do inmates who participate in faith-based programming while in prison have a lower recidivism rate upon their release from prison?

Do police sobriety checkpoints reduce drunken driving fatalities?

What is the impact of a no-smoking policy in prisons on inmate-on-inmate assaults?

Does participation in a domestic violence intervention program reduce repeat domestic violence arrests?

A focus on the classic experimental design will demonstrate the usefulness of this research design for addressing criminal justice questions interested in cause and effect relationships. Particular attention is paid to the classic experimental design because it serves as the foundation for all other experimental and quasi-experimental designs, some of which are covered in this chapter. As a result, a clear understanding of the components, organization, and logic of the classic experimental design will facilitate an understanding of other experimental and quasi-experimental designs examined in this chapter. It will also allow the reader to better understand the results produced from those various designs, and importantly, what those results mean. It is a truism that the results of a research study are only as �good� as the design or method used to produce them. Therefore, understanding the various experimental and quasi-experimental designs is the key to becoming an informed consumer of research.

The Challenge of Establishing Cause and Effect

Researchers interested in explaining the relationship between variables, such as whether a treatment program impacts recidivism, are interested in causation or causal relationships. In a simple example, a causal relationship exists when X (independent variable) causes Y (dependent variable), and there are no other factors (Z) that can explain that relationship. For example, offenders who participated in a domestic violence intervention program (X�domestic violence intervention program) experienced fewer re-arrests (Y�re-arrests) than those who did not participate in the domestic violence program, and no other factor other than participation in the domestic violence program can explain these results. The classic experimental design is superior to other research designs in uncovering a causal relationship, if one exists. Before a causal relationship can be established, however, there are three conditions that must be met (see Figure 5.1). 2

FIGURE 5.1 | The Cause and Effect Relationship

Timing The first condition for a causal relationship is timing. For a causal relationship to exist, it must be shown that the independent variable or cause (X) preceded the dependent variable or outcome (Y) in time. A decrease in domestic violence re-arrests (Y) cannot occur before participation in a domestic violence reduction program (X ), if the domestic violence program is proposed to be the cause of fewer re-arrests. Ensuring that cause comes before effect is not sufficient to establish that a causal relationship exists, but it is one requirement that must be met for a causal relationship.

Association In addition to timing, there must also be an observable association between X and Y, the second necessary condition for a causal relationship. Association is also commonly referred to as covariance or correlation. When an association or correlation exits, this means there is some pattern of relationship between X and Y �as X changes by increasing or decreasing, Y also changes by increasing or decreasing. Here, the notion of X and Y increasing or decreasing can mean an actual increase/decrease in the quantity of some factor, such as an increase/decrease in the number of prison terms or days in a program or re-arrests. It can also refer to an increase/decrease in a particular category, for example, from nonparticipation in a program to participation in a program. For instance, subjects who participated in a domestic violence reduction program (X) incurred fewer domestic violence re-arrests (Y) than those who did not participate in the program. In this example, X and Y are associated�as X change s or increases from nonparticipation to participation in the domestic violence program, Y or the number of re-arrests for domestic violence decreases.

Associations between X and Y can occur in two different directions: positive or negative. A positive association means that as X increases, Y increases, or, as X decreases, Y decreases. A negative association means that as X increases, Y decreases, or, as X decreases, Y increases. In the example above, the association is negative�participation in the domestic violence program was associated with a reduction in re-arrests. This is also sometimes called an inverse relationship.

Elimination of Alternative Explanations Although participation in a domestic violence program may be associated with a reduction in re-arrests, this does not mean for certain that participation in the program was the cause of reduced re-arrests. Just as timing by itself does not imply a causal relationship, association by itself does not imply a causal relationship. For example, instead of the program being the cause of a reduction in re-arrests, perhaps several of the program participants died shortly after completion of the domestic violence program and thus were not able to engage in domestic violence (and their deaths were unknown to the researcher tracking re-arrests). Perhaps a number of the program participants moved out of state and domestic violence re-arrests occurred but were not able to be uncovered by the researcher. Perhaps those in the domestic violence program experienced some other event, such as the trauma of a natural disaster, and that experience led to a reduction in domestic violence, an event not connected to the domestic violence program. If any of these situations occurred, it might appear that the domestic violence program led to fewer re-arrests. However, the observed reduction in re-arrests can actually be attributed to a factor unrelated to the domestic violence program.

The previous discussion leads to the third and final necessary consideration in determining a causal relationship� elimination of alternative explanations. This means that the researcher must rule out any other potential explanation of the results, except for the experimental condition such as a program, policy, or practice. Accounting for or ruling out alternative explanations is much more difficult than ensuring timing and association. Ruling out all alternative explanations is difficult because there are so many potential other explanations that can wholly or partly explain the findings of a research study. This is especially true in the social sciences, where researchers are often interested in relationships explaining human behavior. Because of this difficulty, associations by themselves are sometimes mistaken as causal relationships when in fact they are spurious. A spurious relationship is one where it appears that X and Y are causally related, but the relationship is actually explained by something other than the independent variable, or X.

One only needs to go so far as the daily newspaper to find headlines and stories of mere associations being mistaken, assumed, or represented as causal relationships. For example, a newspaper headline recently proclaimed �Churchgoers live longer.� 3 An uninformed consumer may interpret this headline as evidence of a causal relationship�that going to church by itself will lead to a longer life�but the astute consumer would note possible alternative explanations. For example, people who go to church may live longer because they tend to live healthier lifestyles and tend to avoid risky situations. These are two probable alternative explanations to the relationship independent of simply going to church. In another example, researchers David Kalist and Daniel Yee explored the relationship between first names and delinquent behavior in their manuscript titled �First Names and Crime: Does Unpopularity Spell Trouble?� 4 Kalist and Lee (2009) found that unpopular names are associated with juvenile delinquency. In other words, those individuals with the most unpopular names were more likely to be delinquent than those with more popular names. According to the authors, is it not necessarily someone�s name that leads to delinquent behavior, but rather, the most unpopular names also tend to be correlated with individuals who come from disadvantaged home environments and experience a low socio-economic status of living. Rightly noted by the authors, these alternative explanations help to explain the link between someone�s name and delinquent behavior�a link that is not causal.

A frequently cited example provides more insight to the claim that an association by itself is not sufficient to prove causality. In certain cities in the United States, for example, as ice cream sales increase on a particular day or in a particular month so does the incidence of certain forms of crime. If this association were represented as a causal statement, it would be that ice cream or ice cream sales causes crime. There is an association, no doubt, and let us assume that ice cream sales rose before the increase in crime (timing). Surely, however, this relationship between ice cream sales and crime is spurious. The alternative explanation is that ice cream sales and crime are associated in certain parts of the country because of the weather. Ice cream sales tend to increase in warmer temperatures, and it just so happens that certain forms of crime tend to increase in warmer temperatures as well. This coincidence or association does not mean a causal relationship exists. Additionally, this does not mean that warm temperatures cause crime either. There are plenty of other alternative explanations for the increase in certain forms of crime and warmer temperatures. 6 For another example of a study subject to alternative explanations, read the June 2011 news article titled �Less Crime in U.S. Thanks to Videogames.� 7 Based on your reading, what are some other potential explanations for the crime drop other than videogames?

The preceding examples demonstrate how timing and association can be present, but the final needed condition for a causal relationship is that all alternative explanations are ruled out. While this task is difficult, the classic experimental design helps to ensure these additional explanatory factors are minimized. When other designs are used, such as quasi-experimental designs, the chance that alternative explanations emerge is greater. This potential should become clearer as we explore the organization and logic of the classic experimental design.

CLASSICS IN CJ RESEARCH

Minneapolis Domestic Violence Experiment

The Minneapolis Domestic Violence Experiment (MDVE) 5

Which police action (arrest, separation, or mediation) is most effective at deterring future misdemeanor domestic violence?

The experiment began on March 17, 1981, and continued until August 1, 1982. The experiment was conducted in two of Minneapolis�s four police precincts�the two with the highest number of domestic violence reports and arrests. A total of 314 reports of misdemeanor domestic violence were handled by the police during this time frame.

This study utilized an experimental design with the random assignment of police actions. Each police officer involved in the study was given a pad of report forms. Upon a misdemeanor domestic violence call, the officer�s action (arrest, separation, or mediation) was predetermined by the order and color of report forms in the officer�s notebook. Colored report forms were randomly ordered in the officer�s notebook and the color on the form determined the officer response once at the scene. For example, after receiving a call for domestic violence, an officer would turn to his or her report pad to determine the action. If the top form was pink, the action was arrest. If on the next call the top form was a different color, an action other than arrest would occur. All colored report forms were randomly ordered through a lottery assignment method. The result is that all police officer actions to misdemeanor domestic violence calls were randomly assigned. To ensure the lottery procedure was properly carried out, research staff participated in ride-alongs with officers to ensure that officers did not skip the order of randomly ordered forms. Research staff also made sure the reports were received in the order they were randomly assigned in the pad of report forms.

To examine the relationship of different officer responses to future domestic violence, the researchers examined official arrests of the suspects in a 6-month follow-up period. For example, the researchers examined those initially arrested for misdemeanor domestic violence and how many were subsequently arrested for domestic violence within a 6-month time frame. They did the same procedure for the police actions of separation and mediation. The researchers also interviewed the victim(s) of each incident and asked if a repeat domestic violence incident occurred with the same suspect in the 6-month follow-up period. This allowed researchers to examine domestic violence offenses that may have occurred but did not come to the official attention of police. The researchers then compared official arrests for domestic violence to self-reported domestic violence after the experiment.

Suspects arrested for misdemeanor domestic violence, as opposed to situations where separation or mediation was used, were significantly less likely to engage in repeat domestic violence as measured by official arrest records and victim interviews during the 6-month follow-up period. According to official police records, 10% of those initially arrested engaged in repeat domestic violence in the followup period, 19% of those who initially received mediation engaged in repeat domestic violence, and 24% of those who randomly received separation engaged in repeat domestic violence. According to victim interviews, 19% of those initially arrested engaged in repeat domestic violence, compared to 37% for separation and 33% for mediation. The general conclusion of the experiment was that arrest was preferable to separation or mediation in deterring repeat domestic violence across both official police records and victim interviews.

A few issues that affected the random assignment procedure occurred throughout the study. First, some officers did not follow the randomly assigned action (arrest, separation, or mediation) as a result of other circumstances that occurred at the scene. For example, if the randomly assigned action was separation, but the suspect assaulted the police officer during the call, the officer might arrest the suspect. Second, some officers simply ignored the assigned action if they felt a particular call for domestic violence required another action. For example, if the action was mediation as indicated by the randomly assigned report form, but the officer felt the suspect should be arrested, he or she may have simply ignored the randomly assigned response and substituted his or her own. Third, some officers forgot their report pads and did not know the randomly assigned course of action to take upon a call of domestic violence. Fourth and finally, the police chief also allowed officers to deviate from the randomly assigned action in certain circumstances. In all of these situations, the random assignment procedures broke down.

The results of the MDVE had a rapid and widespread impact on law enforcement practice throughout the United States. Just two years after the release of the study, a 1986 telephone survey of 176 urban police departments serving cities with populations of 100,000 or more found that 46 percent of the departments preferred to make arrests in cases of minor domestic violence, largely due to the effectiveness of this practice in the Minneapolis Domestic Violence Experiment. 8

In an attempt to replicate the findings of the Minneapolis Domestic Violence Experiment, the National Institute of Justice sponsored the Spouse Assault Replication Program. Replication studies were conducted in Omaha, Charlotte, Milwaukee, Miami, and Colorado Springs from 1986�1991. In three of the five replications, offenders randomly assigned to the arrest group had higher levels of continued domestic violence in comparison to other police actions during domestic violence situations. 9 Therefore, rather than providing results that were consistent with the Minneapolis Domestic Violence Experiment, the results from the five replication experiments produced inconsistent findings about whether arrest deters domestic violence. 10

Despite the findings of the replications, the push to arrest domestic violence offenders has continued in law enforcement. Today many police departments require officers to make arrests in domestic violence situations. In agencies that do not mandate arrest, department policy typically states a strong preference toward arrest. State legislatures have also enacted laws impacting police actions regarding domestic violence. Twenty-one states have mandatory arrest laws while eight have pro-arrest statutes for domestic violence. 11

The Classic Experimental Design

Table 5.1 provides an illustration of the classic experimental design. 12 It is important to become familiar with the specific notation and organization of the classic experiment before a full discussion of its components and their purpose.

Major Components of the Classic Experimental Design

The classic experimental design has four major components:

1. Treatment

2. Experimental Group and Control Group

3. Pre-Test and Post-Test

4. Random Assignment

Treatment The first component of the classic experimental design is the treatment, and it is denoted by X in the classic experimental design. The treatment can be a number of things�a program, a new drug, or the implementation of a new policy. In a classic experimental design, the primary goal is to determine what effect, if any, a particular treatment had on some outcome. In this way, the treatment can also be considered the independent variable.

TABLE 5.1 | The Classic Experimental Design

Experimental Group = Group that receives the treatment

Control Group = Group that does not receive the treatment

R = Random assignment

O 1 = Observation before the treatment, or the pre-test

X = Treatment or the independent variable

O 2 = Observation after the treatment, or the post-test

Experimental and Control Groups The second component of the classic experiment is an experimental group and a control group. The experimental group receives the treatment, and the control group does not receive the treatment. There will always be at least one group that receives the treatment in experimental and quasi-experimental designs. In some cases, experiments may have multiple experimental groups receiving multiple treatments.

Pre-Test and Post-Test The third component of the classic experiment is a pre-test and a post-test. A pretest is a measure of the dependent variable or outcome before the treatment. The post-test is a measure of the dependent variable after the treatment is administered. It is important to note that the post-test is defined based on the stated goals of the program. For example, if the stated goal of a particular program is to reduce re-arrests, the post-test will be a measure of re-arrests after the program. The dependent variable also defines the pre-test. For example, if a researcher wanted to examine the impact of a domestic violence reduction program (treatment or X) on the goal of reducing re-arrests (dependent variable or Y), the pre-test would be the number of domestic violence arrests incurred before the program. Program goals may be numerous and all can constitute a post-test, and hence, the pre-test. For example, perhaps the goal of the domestic violence program is also that participants learn of different pro-social ways to handle domestic conflicts other than resorting to violence. If researchers wanted to examine this goal, the post-test might be subjects� level of knowledge about pro-social ways to handle domestic conflicts other than violence. The pre-test would then be subjects� level of knowledge about these pro-social alternatives to violence before they received the treatment program.

Although all designs have a post-test, it is not always the case that designs have a pre-test. This is because researchers may not have access or be able to collect information constituting the pre-test. For example, researchers may not be able to determine subjects� level of knowledge about alternatives to domestic violence before the intervention program if the subjects are already enrolled in the domestic violence intervention program. In other cases, there may be financial barriers to collecting pre-test information. In the teen court evaluation that started this chapter, for example, researchers were not able to collect pre-test information on study participants due to the financial strain it would have placed on the agencies involved in the study. 13 There are a number of potential reasons why a pre-test might not be available in a research study. The defining feature, however, is that the pre-test is determined by the post-test.

Random Assignment The fourth component of the classic experiment is random assignment. Random assignment refers to a process whereby members of the experimental group and control group are assigned to the two groups through a random and unbiased process. Random assignment should not be mistaken for random selection as discussed in Chapter 3. Random selection refers to selecting a smaller but representative sample from a larger population. For example, a researcher may randomly select a sample from a larger city population for the purposes of sending sample members a mail survey to determine their attitudes on crime. The goal of random selection in this example is to make sure the sample, although smaller in size than the population, accurately represents the larger population.

Random assignment, on the other hand, refers to the process of assigning subjects to either the experimental or control group with the goal that the groups are similar or equivalent to each other in every way (see Figure 5.2). The exception to this rule is that one group gets the treatment and the other does not (see discussion below on why equivalence is so important). Although the concept of random is similar in each, the goals are different between random selection and random assignment. 14 Experimental designs all feature random assignment, but this is not true of other research designs, in particular quasi-experimental designs.

FIGURE 5.2 | Random Assignment

The classic experimental design is the foundation for all other experimental and quasi-experimental designs because it retains all of the major components discussed above. As mentioned, sometimes designs do not have a pre-test, a control group, or random assignment. Because the pre-test, control group, and random assignment are so critical to the goal of uncovering a causal relationship, if one exists, we explore them further below.

The Logic of the Classic Experimental Design

Consider a research study using the classic experimental design where the goal is to determine if a domestic violence treatment program has any effect on re-arrests for domestic violence. The randomly assigned experimental and control groups are comprised of persons who had previously been arrested for domestic violence. The pretest is a measure of the number of domestic violence arrests before the program. This is because the goal of the program is to determine whether re-arrests are impacted after the treatment. The post-test is the number of re-arrests following the treatment program.

Once randomly assigned, the experimental group members receive the domestic violence program, and the control group members do not. After the program, the researcher will compare the pre-test arrests for domestic violence of the experimental group to post-test arrests for domestic violence to determine if arrests increased, decreased, or remained constant since the start of the program. The researcher will also compare the post-test re-arrests for domestic violence between the experimental and control groups. With this example, we explore the usefulness of the classic experimental design, and the contribution of the pre-test, random assignment, and the control group to the goal of determining whether a domestic violence program reduces re-arrests.

The Pre-Test As a component of the classic experiment, the pre-test allows an examination of change in the dependent variable from before the domestic violence program to after the domestic violence program. In short, a pre-test allows the researcher to determine if re-arrests increased, decreased, or remained the same following the domestic violence program. Without a pre-test, researchers would not be able to determine the extent of change, if any, from before to after the program for either the experimental or control group.

Although the pre-test is a measure of the dependent variable before the treatment, it can also be thought of as a measure whereby the researcher can compare the experimental group to the control group before the treatment is administered. For example, the pre-test helps researchers to make sure both groups are similar or equivalent on previous arrests for domestic violence. The importance of equivalence between the experimental and control groups on previous arrests is discussed below with random assignment.

Random Assignment Random assignment helps to ensure that the experimental and control groups are equivalent before the introduction of the treatment. This is perhaps one of the most critical aspects of the classic experiment and all experimental designs. Although the experimental and control groups will be made up of different people with different characteristics, assigning them to groups via a random assignment process helps to ensure that any differences or bias between the groups is eliminated or minimized. By minimizing bias, we mean that the groups will balance each other out on all factors except the treatment. If they are balanced out on all factors prior to the administration of the treatment, any differences between the groups at the post-test must be due to the treatment�the only factor that differs between the experimental group and the control group. According to Shadish, Cook, and Campbell: �If implemented correctly, random assignment creates two or more groups of units that are probabilistically similar to each other on the average. Hence, any outcome differences that are observed between those groups at the end of a study are likely to be due to treatment, not to differences between the groups that already existed at the start of the study.� 15 Considered in another way, if the experimental and control group differed significantly on any relevant factor other than the treatment, the researcher would not know if the results observed at the post-test are attributable to the treatment or to the differences between the groups.

Consider an example where 500 domestic abusers were randomly assigned to the experimental group and 500 were randomly assigned to the control group. Because they were randomly assigned, we would likely find more frequent domestic violence arrestees in both groups, older and younger arrestees in both groups, and so on. If random assignment was implemented correctly, it would be highly unlikely that all of the experimental group members were the most serious or frequent arrestees and all of the control group members were less serious and/or less frequent arrestees. While there are no guarantees, we know the chance of this happening is extremely small with random assignment because it is based on known probability theory. Thus, except for a chance occurrence, random assignment will result in equivalence between the experimental and control group in much the same way that flipping a coin multiple times will result in heads approximately 50% of the time and tails approximately 50% of the time. Over 1,000 tosses of a coin, for example, should result in roughly 500 heads and 500 tails. While there is a chance that flipping a coin 1,000 times will result in heads 1,000 times, or some other major imbalance between heads and tails, this potential is small and would only occur by chance.

The same logic from above also applies with randomly assigning people to groups, and this can even be done by flipping a coin. By assigning people to groups through a random and unbiased process, like flipping a coin, only by chance (or researcher error) will one group have more of one characteristic than another, on average. If there are no major (also called statistically significant) differences between the experimental and control group before the treatment, the most plausible explanation for the results at the post-test is the treatment.

As mentioned, it is possible by some chance occurrence that the experimental and control group members are significantly different on some characteristic prior to administration of the treatment. To confirm that the groups are in fact similar after they have been randomly assigned, the researcher can examine the pre-test if one is present. If the researcher has additional information on subjects before the treatment is administered, such as age, or any other factor that might influence post-test results at the end of the study, he or she can also compare the experimental and control group on those measures to confirm that the groups are equivalent. Thus, a researcher can confirm that the experimental and control groups are equivalent on information known to the researcher.

Being able to compare the groups on known measures is an important way to ensure the random assignment process �worked.� However, perhaps most important is that randomization also helps to ensure similarity across unknown variables between the experimental and control group. Because random assignment is based on known probability theory, there is a much higher probability that all potential differences between the groups that could impact the post-test should balance out with random assignment�known or unknown. Without random assignment, it is likely that the experimental and control group would differ on important but unknown factors and such differences could emerge as alternative explanations for the results. For example, if a researcher did not utilize random assignment and instead took the first 500 domestic abusers from an ordered list and assigned them to the experimental group and the last 500 domestic abusers and assigned them to the control group, one of the groups could be �lopsided� or imbalanced on some important characteristic that could impact the outcome of the study. With random assignment, there is a much higher likelihood that these important characteristics among the experimental and control groups will balance out because no individual has a different chance of being placed into one group versus the other. The probability of one or more characteristics being concentrated into one group and not the other is extremely small with random assignment.

To further illustrate the importance of random assignment to group equivalence, suppose the first 500 domestic violence abusers who were assigned to the experimental group from the ordered list had significantly fewer domestic violence arrests before the program than the last 500 domestic violence abusers on the list. Perhaps this is because the ordered list was organized from least to most chronic domestic abusers. In this instance, the control group would be lopsided concerning number of pre-program domestic violence arrests�they would be more chronic than the experimental group. The arrest imbalance then could potentially explain the post-test results following the domestic violence program. For example, the �less risky� offenders in the experimental group might be less likely to be re-arrested regardless of their participation in the domestic violence program, especially compared to the more chronic domestic abusers in the control group. Because of imbalances between the experimental and control group on arrests before the program was implemented, it would not be known for certain whether an observed reduction in re-arrests after the program for the experimental group was due to the program or the natural result of having less risky offenders in the experimental group. In this instance, the results might be taken to suggest that the program significantly reduces re-arrests. This conclusion might be spurious, however, for the association may simply be due to the fact that the offenders in the experimental group were much different (less frequent offenders) than the control group. Here, the program may have had no effect�the experimental group members may have performed the same regardless of the treatment because they were low-level offenders.

The example above suggests that differences between the experimental and control groups based on previous arrest records could have a major impact on the results of a study. Such differences can arise with the lack of random assignment. If subjects were randomly assigned to the experimental and control group, however, there would be a much higher probability that less frequent and more frequent domestic violence arrestees would have been found in both the experimental and control groups and the differences would have balanced out between the groups�leaving any differences between the groups at the post-test attributable to the treatment only.

In summary, random assignment helps to ensure that the experimental and control group members are balanced or equivalent on all factors that could impact the dependent variable or post-test�known or unknown. The only factor they are not balanced or equal on is the treatment. As such, random assignment helps to isolate the impact of the treatment, if any, on the post-test because it increases confidence that the only difference between the groups should be that one group gets the treatment and the other does not. If that is the only difference between the groups, any change in the dependent variable between the experimental and control group must be attributed to the treatment and not an alternative explanation, such as significant arrest history imbalance between the groups (refer to Figure 5.2). This logic also suggests that if the experimental group and control group are imbalanced on any factor that may be relevant to the outcome, that factor then becomes a potential alternative explanation for the results�an explanation that reduces the researcher�s ability to isolate the real impact of the treatment.

WHAT RESEARCH SHOWS: IMPACTING CRIMINAL JUSTICE OPERATIONS

Scared Straight

The 1978 documentary Scared Straight introduced to the public the �Lifer�s Program� at Rahway State Prison in New Jersey. This program sought to decrease juvenile delinquency by bringing at-risk and delinquent juveniles into the prison where they would be �scared straight� by inmates serving life sentences. Participants in the program were talked to and yelled at by the inmates in an effort to scare them. It was believed that the fear felt by the participants would lead to a discontinuation of their problematic behavior so that they would not end up in prison themselves. Although originally touted as a success based on anecdotal evidence, subsequent evaluations of the program and others like it proved otherwise.

Using a classic experimental design, Finckenauer evaluated the original �Lifer�s Program� at Rahway State Prison. 16 Participating juveniles were randomly assigned to the experimental group or the control group. Results of the evaluation were not positive. Post-test measures revealed that juveniles who were assigned to the experimental group and participated in the program were actually more seriously delinquent afterwards than those who did not participate in the program. Also using an experimental design with random assignment, Yarborough evaluated the �Juvenile Offenders Learn Truth� (JOLT) program at the State Prison of Southern Michigan at Jackson. 17 This program was similar to that of the �Lifer�s Program� only with fewer obscenities used by the inmates. Post-test measurements were taken at two intervals, 3 and 6 months after program completion. Again, results were not positive. Findings revealed no significant differences between those juveniles who attended the program and those who did not.

Other experiments conducted on Scared Straight -like programs further revealed their inability to deter juveniles from future criminality. 18 Despite the intuitive popularity of these programs, these evaluations proved that such programs were not successful. In fact, it is postulated that these programs may have actually done more harm than good.

The Control Group The presence of an equivalent control group (created through random assignment) also gives the researcher more confidence that the findings at the post-test are due to the treatment and not some other alternative explanation. This logic is perhaps best demonstrated by considering how interpretation of results is affected without a control group. Absent an equivalent control group, it cannot be known whether the results of the study are due to the program or some other factor. This is because the control group provides a baseline of comparison or a �control.� For example, without a control group, the researcher may find that domestic violence arrests declined from pre-test to post-test. But the researcher would not be able to definitely attribute that finding to the program without a control group. Perhaps the single experimental group incurred fewer arrests because they matured over their time in the program, regardless of participation in the domestic violence program. Having a randomly assigned control group would allow this consideration to be eliminated, because the equivalent control group would also have naturally matured if that was the case.

Because the control group is meant to be similar to the experimental group on all factors with the exception that the experimental group receives the treatment, the logic is that any differences between the experimental and control group after the treatment must then be attributable only to the treatment itself�everything else occurs equally in both the experimental and control groups and thus cannot be the cause of results. The bottom line is that a control group allows the researcher more confidence to attribute any change in the dependent variable from pre- to post-test and between the experimental and control groups to the treatment�and not another alternative explanation. Absent a control group, the researcher would have much less confidence in the results.

Knowledge about the major components of the classic experimental design and how they contribute to an understanding of cause and effect serves as an important foundation for studying different types of experimental and quasi-experimental designs and their organization. A useful way to become familiar with the components of the experimental design and their important role is to consider the impact on the interpretation of results when one or more components are lacking. For example, what if a design lacked a pre-test? How could this impact the interpretation of post-test results and knowledge about the comparability of the experimental and control group? What if a design lacked random assignment? What are some potential problems that could occur and how could those potential problems impact interpretation of results? What if a design lacked a control group? How does the absence of an equivalent control group affect a researcher�s ability to determine the unique effects of the treatment on the outcomes being measured? The ability to discuss the contribution of a pre-test, random assignment, and a control group�and what is the impact when one or more of those components is absent from a research design�is the key to understanding both experimental and quasi-experimental designs that will be discussed in the remainder of this chapter. As designs lose these important parts and transform from a classic experiment to another experimental design or to a quasi-experiment, they become less useful in isolating the impact that a treatment has on the dependent variable and allow more room for alternative explanations of the results.

One more important point must be made before further delving into experimental and quasi-experimental designs. This point is that rarely, if ever, will the average consumer of research be exposed to the symbols or specific language of the classic experiment, or other experimental and quasi-experimental designs examined in this chapter. In fact, it is unlikely that the average consumer will ever be exposed to the terms pre-test, post-test, experimental group, or random assignment in the popular media, among other terms related to experimental and quasi-experimental designs. Yet, consumers are exposed to research results produced from these and other research designs every day. For example, if a national news organization or your regional newspaper reported a story about the effectiveness of a new drug to reduce cholesterol or the effects of different diets on weight loss, it is doubtful that the results would be reported as produced through a classic experimental design that used a control group and random assignment. Rather, these media outlets would use generally nonscientific terminology such as �results of an experiment showed� or �results of a scientific experiment indicated� or �results showed that subjects who received the new drug had greater cholesterol reductions than those who did not receive the new drug.� Even students who regularly search and read academic articles for use in course papers and other projects will rarely come across such design notation in the research studies they utilize. Depiction of the classic experimental design, including a discussion of its components and their function, simply illustrates the organization and notation of the classic experimental design. Unfortunately, the average consumer has to read between the lines to determine what type of design was used to produce the reported results. Understanding the key components of the classic experimental design allows educated consumers of research to read between those lines.

RESEARCH IN THE NEWS

�Swearing Makes Pain More Tolerable� 19

In 2009, Richard Stephens, John Atkins, and Andrew Kingston of the School of Psychology at Keele University conducted a study with 67 undergraduate students to determine if swearing affects an individual�s response to pain. Researchers asked participants to immerse their hand in a container filled with ice-cold water and repeat a preferred swear word. The researchers then asked the same participants to immerse their hand in ice-cold water while repeating a word used to describe a table (a non-swear word). The results showed that swearing increased pain tolerance compared to the non-swearing condition. Participants who used a swear word were able to hold their hand in ice-cold water longer than when they did not swear. Swearing also decreased participants� perception of pain.

1. This study is an example of a repeated measures design. In this form of experimental design, study participants are exposed to an experimental condition (swearing with hand in ice-cold water) and a control condition (non-swearing with hand in ice-cold water) while repeated outcome measures are taken with each condition, for example, the length of time a participant was able to keep his or her hand submerged in ice-cold water. Conduct an Internet search for �repeated measures design� and explore the various ways such a study could be conducted, including the potential benefits and drawbacks to this design.

2. After researching repeated measures designs, devise a hypothetical repeated measures study of your own.

3. Retrieve and read the full research study �Swearing as a Response to Pain� by Stephens, Atkins, and Kingston while paying attention to the design and methods (full citation information for this study is listed below). Has your opinion of the study results changed after reading the full study? Why or why not?

Full Study Source: Stephens, R., Atkins, J., and Kingston, A. (2009). �Swearing as a response to pain.� NeuroReport 20, 1056�1060.

Variations on the Experimental Design

The classic experimental design is the foundation upon which all experimental and quasi-experimental designs are based. As such, it can be modified in numerous ways to fit the goals (or constraints) of a particular research study. Below are two variations of the experimental design. Again, knowledge about the major components of the classic experiment, how they contribute to an explanation of results, and what the impact is when one or more components are missing provides an understanding of all other experimental designs.

Post-Test Only Experimental Design

The post-test only experimental design could be used to examine the impact of a treatment program on school disciplinary infractions as measured or operationalized by referrals to the principal�s office (see Table 5.2). In this design, the researcher randomly assigns a group of discipline problem students to the experimental group and control group by flipping a coin�heads to the experimental group and tails to the control group. The experimental group then enters the 3-month treatment program. After the program, the researcher compares the number of referrals to the principal�s office between the experimental and control groups over some period of time, for example, discipline referrals at 6 months after the program. The researcher finds that the experimental group has a much lower number of referrals to the principal�s office in the 6 month follow-up period than the control group.

TABLE 5.2 | Post-Test Only Experimental Design

Several issues arise in this example study. The researcher would not know if discipline problems decreased, increased, or stayed the same from before to after the treatment program because the researcher did not have a count of disciplinary referrals prior to the treatment program (e.g., a pre-test). Although the groups were randomly assigned and are presumed equivalent, the absence of a pre-test means the researcher cannot confirm that the experimental and control groups were equivalent before the treatment was administered, particularly on the number of referrals to the principal�s office. The groups could have differed by a chance occurrence even with random assignment, and any such differences between the groups could potentially explain the post-test difference in the number of referrals to the principal�s office. For example, if the control group included much more serious or frequent discipline problem students than the experimental group by chance, this difference might explain the lower number of referrals for the experimental group, not that the treatment produced this result.

Experimental Design with Two Treatments and a Control Group

This design could be used to determine the impact of boot camp versus juvenile detention on post-release recidivism (see Table 5.3). Recidivism in this study is operationalized as re-arrest for delinquent behavior. First, a population of known juvenile delinquents is randomly assigned to either boot camp, juvenile detention, or a control condition where they receive no sanction. To accomplish random assignment to groups, the researcher places the names of all youth into a hat and assigns the groups in order. For example, the first name pulled goes into experimental group 1, the next into experimental group 2, and the next into the control group, and so on. Once randomly assigned, the experimental group youth receive either boot camp or juvenile detention for a period of 3 months, whereas members of the control group are released on their own recognizance to their parents. At the end of the experiment, the researcher compares the re-arrest activity of boot camp participants to detention delinquents to control group members during a 6-month follow-up period.

TABLE 5.3 | Experimental Design with Two Treatments and a Control Group

This design has several advantages. First, it includes all major components of the classic experimental design, and simply adds an additional treatment for comparison purposes. Random assignment was utilized and this means that the groups have a higher probability of being equivalent on all factors that could impact the post-test. Thus, random assignment in this example helps to ensure the only differences between the groups are the treatment conditions. Without random assignment, there is a greater chance that one group of youth was somehow different, and this difference could impact the post-test. For example, if the boot camp youth were much less serious and frequent delinquents than the juvenile detention youth or control group youth, the results might erroneously show that the boot camp reduced recidivism when in fact the youth in boot camp may have been the �best risks��unlikely to get re-arrested with or without boot camp. The pre-test in the example above allows the researcher to determine change in re-arrests from pretest to post-test. Thus, the researcher can determine if delinquent behavior, as measured by re-arrest, increased, decreased, or remained constant from pre- to post-test. The pre-test also allows the researcher to confirm that the random assignment process resulted in equivalent groups based on the pre-test. Finally, the presence of a control group allows the researcher to have more confidence that any differences in the post-test are due to the treatment. For example, if the control group had more re-arrests than the boot camp or juvenile detention experimental groups 6 months after their release from those programs, the researcher would have more confidence that the programs produced fewer re-arrests because the control group members were the same as the experimental groups; the only difference was that they did not receive a treatment.

The one key feature of experimental designs is that they all retain random assignment. This is why they are considered �experimental� designs. Sometimes, however, experimental designs lack a pre-test. Knowledge of the usefulness of a pre-test demonstrates the potential problems with those designs where it is missing. For example, in the post-test only experimental design, a researcher would not be able to make a determination of change in the dependent variable from pre- to post-test. Perhaps most importantly, the researcher would not be able to confirm that the experimental and control groups were in fact equivalent on a pre-test measure before the introduction of the treatment. Even though both groups were randomly assigned, and probability theory suggests they should be equivalent, without a pre-test measure the researcher could not confirm similarity because differences could occur by chance even with random assignment. If there were any differences at the post-test between the experimental group and control group, the results might be due to some explanation other than the treatment, namely that the groups differed prior to the administration of the treatment. The same limitation could apply in any form of experimental design that does not utilize a pre-test for conformational purposes.

Understanding the contribution of a pre-test to an experimental design shows that it is a critical component. It provides a measure of change and also gives the researcher more confidence that the observed results are due to the treatment, and not some difference between the experimental and control groups. Despite the usefulness of a pre-test, however, perhaps the most critical ingredient of any experimental design is random assignment. It is important to note that all experimental designs retain random assignment.

Experimental Designs Are Rare in Criminal Justice and Criminology

The classic experiment is the foundation for other types of experimental and quasi-experimental designs. The unfortunate reality, however, is that the classic experiment, or other experimental designs, are few and far between in criminal justice. 20 Recall that one of the major components of an experimental design is random assignment. Achieving random assignment is often a barrier to experimental research in criminal justice. Achieving random assignment might, for example, require the approval of the chief (or city council or both) of a major metropolitan police agency to allow researchers to randomly assign patrol officers to certain areas of a city and/or randomly assign police officer actions. Recall the MDVE. This experiment required the full cooperation of the chief of police and other decision-makers to allow researchers to randomly assign police actions. In another example, achieving random assignment might require a judge to randomly assign a group of youthful offenders to a certain juvenile court sanction (experimental group), and another group of similar youthful offenders to no sanction or an alternative sanction as a control group. 21 In sum, random assignment typically requires the cooperation of a number of individuals and sometimes that cooperation is difficult to obtain.

Even when random assignment can be accomplished, sometimes it is not implemented correctly and the random assignment procedure breaks down. This is another barrier to conducting experimental research. For example, in the MDVE, researchers randomly assigned officer responses, but the officers did not always follow the assigned course of action. Moreover, some believe that the random assignment of criminal justice programs, sentences, or randomly assigning officer responses may be unethical in certain circumstances, and even a violation of the rights of citizens. For example, some believe it is unfair when random assignment results in some delinquents being sentenced to boot camp while others get assigned to a control group without any sanction at all or a less restrictive sanction than boot camp. In the MDVE, some believe it is unfair that some suspects were arrested and received an official record whereas others were not arrested for the same type of behavior. In other cases, subjects in the experimental group may receive some benefit from the treatment that is essentially denied to the control group for a period of time and this can become an issue as well.

There are other important reasons why random assignment is difficult to accomplish. Random assignment may, for example, involve a disruption of the normal procedures of agencies and their officers. In the MDVE, officers had to adjust their normal and established routine, and this was a barrier at times in that study. Shadish, Cook, and Campbell also note that random assignment may not always be feasible or desirable when quick answers are needed. 22 This is because experimental designs sometimes take a long time to produce results. In addition to the time required in planning and organizing the experiment, and treatment delivery, researchers may need several months if not years to collect and analyze the data before they have answers. This is particularly important because time is often of the essence in criminal justice research, especially in research efforts testing the effect of some policy or program where it is not feasible to wait years for answers. Waiting for the results of an experimental design means that many policy-makers may make decisions without the results.

Quasi-Experimental Designs

In general terms, quasi-experiments include a group of designs that lack random assignment. Quasi-experiments may also lack other parts, such as a pre-test or a control group, just like some experimental designs. The absence of random assignment, however, is the ingredient that transforms an otherwise experimental design into a quasi-experiment. Lacking random assignment is a major disadvantage because it increases the chances that the experimental and control groups differ on relevant factors before the treatment�both known and unknown�differences that may then emerge as alternative explanations of the outcomes.

Just like experimental designs, quasi-experimental designs can be organized in many different ways. This section will discuss three types of quasi-experiments: nonequivalent group design, one-group longitudinal design, and two-group longitudinal design.

Nonequivalent Group Design

The nonequivalent group design is perhaps the most common type of quasi-experiment. 23 Notice that it is very similar to the classic experimental design with the exception that it lacks random assignment (see Table 5.4). Additionally, what was labeled the experimental group in an experimental design is sometimes called the treatment group in the nonequivalent group design. What was labeled the control group in the experimental design is sometimes called the comparison group in the nonequivalent group design. This terminological distinction is an indicator that the groups were not created through random assignment.

TABLE 5.4 | Nonequivalent Group Design

NR = Not Randomly assigned

One of the main problems with the nonequivalent group design is that it lacks random assignment, and without random assignment, there is a greater chance that the treatment and comparison groups may be different in some way that can impact study results. Take, for example, a nonequivalent group design where a researcher is interested in whether an aggression-reduction treatment program can reduce inmate-on-inmate assaults in a prison setting. Assume that the researcher asked for inmates who had previously been involved in assaultive activity to volunteer for the aggression-reduction program. Suppose the researcher placed the first 50 volunteers into the treatment group and the next 50 volunteers into the comparison group. Note that this method of assignment is not random but rather first come, first serve.

Because the study utilized volunteers and there was no random assignment, it is possible that the first 50 volunteers placed into the treatment group differed significantly from the last 50 volunteers who were placed in the comparison group. This can lead to alternative explanations for the results. For example, if the treatment group was much younger than the comparison group, the researcher may find at the end of the program that the treatment group still maintained a higher rate of infractions than the comparison group�even after the aggression-reduction program! The conclusion might be that the aggression program actually increased the level of violence among the treatment group. This conclusion would likely be spurious and may be due to the age differential between the treatment and comparison groups. Indeed, research has revealed that younger inmates are significantly more likely to engage in prison assaults than older inmates. The fact that the treatment group incurred more assaults than the comparison group after the aggression-reduction program may only relate to the age differential between the groups, not that the program had no effect or that it somehow may have increased aggression. The previous example highlights the importance of random assignment and the potential problems that can occur in its absence.

Although researchers who utilize a quasi-experimental design are not able to randomly assign their subjects to groups, they can employ other techniques in an attempt to make the groups as equivalent as possible on known or measured factors before the treatment is given. In the example above, it is likely that the researcher would have known the age of inmates, their prior assault record, and various other pieces of information (e.g., previous prison stays). Through a technique called matching, the researcher could make sure the treatment and comparison groups were �matched� on these important factors before administering the aggression reduction program to the treatment group. This type of matching can be done individual to individual (e.g., subject #1 in treatment group is matched to a selected subject #1 in comparison group on age, previous arrests, gender), or aggregately, such that the comparison group is similar to the treatment group overall (e.g., average ages between groups are similar, equal proportions of males and females). Knowledge of these and other important variables, for example, would allow the researcher to make sure that the treatment group did not have heavy concentrations of younger or more frequent or serious offenders than the comparison group�factors that are related to assaultive activity independent of the treatment program. In short, matching allows the researcher some control over who goes into the treatment and comparison groups so as to balance these groups on important factors absent random assignment. If unbalanced on one or more factors, these factors could emerge as alternative explanations of the results. Figure 5.3 demonstrates the logic of matching both at the individual and aggregate level in a quasi-experimental design.

Matching is an important part of the nonequivalent group design. By matching, the researcher can approximate equivalence between the groups on important variables that may influence the post-test. However, it is important to note that a researcher can only match subjects on factors that they have information about�a researcher cannot match the treatment and comparison group members on factors that are unmeasured or otherwise unknown but which may still impact outcomes. For example, if the researcher has no knowledge about the number of previous incarcerations, the researcher cannot match the treatment and comparison groups on this factor. Matching also requires that the information used for matching is valid and reliable, which is not always the case. Agency records, for example, are notorious for inconsistencies, errors, omissions, and for being dated, but are often utilized for matching purposes. Asking survey questions to generate information for matching (for example, how many times have you been incarcerated?) can also be problematic because some respondents may lie, forget, or exaggerate their behavior or experiences.

In addition to the above considerations, the more factors a researcher wishes to match the group members on, the more difficult it becomes to find appropriate matches. Matching on prior arrests or age is less complex than matching on several additional pieces of information. Finally, matching is never considered superior to random assignment when the goal is to construct equitable groups. This is because there is a much higher likelihood of equivalence with random assignment on factors that are both measured and unknown to the researcher. Thus, the results produced from a nonequivalent group design, even with matching, are at a greater risk of alternative explanations than an experimental design that features random assignment.

FIGURE 5.3 | (a) Individual Matching (b) Aggregate Matching

The previous discussion is not to suggest that the nonequivalent group design cannot be useful in answering important research questions. Rather, it is to suggest that the nonequivalent group design, and hence any quasi-experiment, is more susceptible to alternative explanations than the classic experimental design because of the absence of random assignment. As a result, a researcher must be prepared to rule out potential alternative explanations. Quasi-experimental designs that lack a pre-test or a comparison group are even less desirable than the nonequivalent group design and are subject to additional alternative explanations because of these missing parts. Although the quasi-experiment may be all that is available and still can serve as an important design in evaluating the impact of a particular treatment, it is not preferable to the classic experiment. Researchers (and consumers) must be attuned to the potential issues of this design so as to make informed conclusions about the results produced from such research studies.

The Effects of Red Light Camera (RLC) Enforcement

On March 15, 2009, an article appeared in the Santa Cruz Sentinel entitled �Ticket�s in the Mail: Red-Light Cameras Questioned.� The article stated �while studies show fewer T-bone crashes at lights with cameras and fewer drivers running red lights, the number of rear-end crashes increases.� 24 The study mentioned in the newspaper, which showed fewer drivers running red lights with cameras, was conducted by Richard Retting, Susan Ferguson, and Charles Farmer of the Insurance Institute for Highway Safety (IIHS). 25 They completed a quasi-experimental study in Philadelphia to determine the impact of red light cameras (RLC) on red light violations. In the study, the researchers selected nine intersections�six of which were experimental sites that utilized RLCs and three comparison sites that did not utilize RLCs. The six experimental sites were located in Philadelphia, Pennsylvania, and the three comparison sites were located in Atlantic County, New Jersey. The researchers chose the comparison sites based on the proximity to Philadelphia, the ability to collect data using the same methods as at experimental intersections (e.g., the use of cameras for viewing red light traffic), and the fact that police officials in Atlantic County had offered assistance selecting and monitoring the intersections.

The authors collected three phases of information in the RLC study at the experimental and comparison sites:

Phase 1 Data Collection: Baseline (pre-test) data collection at the experimental and comparison sites consisting of the number of vehicles passing through each intersection, the number of red light violations, and the rate of red light violations per 10,000 vehicles.

Phase 2 Data Collection: Number of vehicles traveling through experimental and comparison intersections, number of red light violations after a 1-second yellow light increase at the experimental sites (treatment 1), number of red light violations at comparison sites without a 1-second yellow light increase, and red light violations per 10,000 vehicles at both experimental and comparison sites.

Phase 3 Data Collection: Red light violations after a 1-second yellow light increase and RLC enforcement at the experimental sites (treatment 2), red light violations at comparison sites without a 1-second yellow increase or RLC enforcement, number of vehicles passing through the experimental and comparison intersections, and the rate of red light violations per 10,000 vehicles.

The researchers operationalized �red light violations� as those where the vehicle entered the intersection one-half of a second or more after the onset of the red signal where the vehicle�s rear tires had to be positioned behind the crosswalk or stop line prior to entering on red. Vehicles already in the intersection at the onset of the red light, or those making a right turn on red with or without stopping were not considered red light violations.

The researchers collected video data at each of the experimental and comparison sites during Phases 1�3. This allowed the researchers to examine red light violations before, during, and after the implementation of red light enforcement and yellow light time increases. Based on an analysis of data, the researchers revealed that the implementation of a 1-second yellow light increase led to reductions in the rate of red light violations from Phase 1 to Phase 2 in all of the experimental sites. In 2 out of 3 comparison sites, the rate of red light violations also decreased, despite no yellow light increase. From Phase 2 to Phase 3 (the enforcement of red light camera violations in addition to a 1-second yellow light increase at experimental sites), the authors noted decreases in the rate of red light violations in all experimental sites, and decreases among 2 of 3 comparison sites without red light enforcement in effect.

Concluding their study, the researchers noted that the study �found large and highly significant incremental reductions in red light running associated with increased yellow signal timing followed by the introduction of red light cameras.� Despite these findings, the researchers noted a number of potential factors to consider in light of the findings: the follow-up time periods utilized when counting red light violations before and after the treatment conditions were instituted; publicity about red light camera enforcement; and the size of fines associated with red light camera enforcement (the fine in Philadelphia was $100, higher than in many other cities), among others.

After reading about the study used in the newspaper article, has your impression of the newspaper headline and quote changed?

For more information and research on the effect of RLCs, visit the Insurance Institute for Highway Safety at http://www .iihs.org/research/topics/rlr.html .

One-Group Longitudinal Design

Like all experimental designs, the quasi-experimental design can come in a variety of forms. The second quasi-experimental design (above) is the one-group longitudinal design (also called a simple interrupted time series design). 26 An examination of this design shows that it lacks both random assignment and a comparison group (see Table 5.5). A major difference between this design and others we have covered is that it includes multiple pre-test and post-test observations.

TABLE 5.5 | One-Group Longitudinal Design

The one-group longitudinal design is useful when researchers are interested in exploring longer-term patterns. Indeed, the term longitudinal generally means �over time��repeated measurements of the pre-test and post-test over time. This is different from cross-sectional designs, which examine the pre-test and post-test at only one point in time (e.g., at a single point before the application of the treatment and at a single point after the treatment). For example, in the nonequivalent group design and the classic experimental design previously examined, both are cross-sectional because pre-tests and post-tests are measured at one point in time (e.g., at a point 6 months after the treatment). Yet, these designs could easily be considered longitudinal if researchers took repeated measures of the pre-test and post-test.

The organization of the one-group longitudinal design is to examine a baseline of several pre-test observations, introduce a treatment or intervention, and then examine the post-test at several different time intervals. As organized, this design is useful for gauging the impact that a particular program, policy, or law has, if any, and how long the treatment impact lasts. Consider an example whereby a researcher is interested in gauging the impact of a tobacco ban on inmate-on-inmate assaults in a prison setting. This is an important question, for recent years have witnessed correctional systems banning all tobacco products from prison facilities. Correctional administrators predicted that there would be a major increase of inmate-on-inmate violence once the bans took effect. The one-group longitudinal design would be one appropriate design to examine the impact of banning tobacco on inmate assaults.

To construct this study using the one-group longitudinal design, the researcher would first examine the rate of inmate-on-inmate assaults in the prison system (or at an individual prison, a particular cellblock, or whatever the unit of analysis) prior to the removal of tobacco. This is the pre-test, or a baseline of assault activity before the ban goes into effect. In the design presented above, perhaps the researcher would measure the level of assaults in the preceding four months prior to the tobacco ban. When establishing a pre-test baseline, the general rule is that, in a longitudinal design, the more time utilized, both in overall time and number of intervals, the better. For example, the rate of assaults in the preceding month is not as useful as an entire year of data on inmate assaults prior to the tobacco ban. Next, once the tobacco ban is implemented, the researcher would then measure the rate of inmate assaults in the coming months to determine what impact the ban had on inmate-on-inmate assaults. This is shown in Table 5.5 as the multiple post-test measures of assaults. Assaults may increase, decrease, or remain constant from the pre-test baseline over the term of the post-test.

If assaults increased at the same time as the ban went into effect, the researcher might conclude that the increase was due only to the tobacco ban. But, could there be alternative explanations? The answer to this question is yes, there may be other plausible explanations for the increase even with several months of pre-test data. Unfortunately, without a comparison group there is no way for the researcher to be certain if the increase in assaults was due to the tobacco ban, or some other factor that may have spurred the increase in assaults and happened at the same time as the tobacco ban. What if assaults decreased after the tobacco ban went into effect? In this scenario, because there is no comparison group, the researcher would still not know if the results would have happened anyway without the tobacco ban. In these instances, the lack of a comparison group prevents the researcher from confidently attributing the results to the tobacco ban, and interpretation is subject to numerous alternative explanations.

Two-Group Longitudinal Design

A remedy for the previous situation would be to introduce a comparison group (see Table 5.6). Prior to the full tobacco ban, suppose prison administrators conducted a pilot program at one prison to provide insight as to what would happen once the tobacco ban went into effect systemwide. To conduct this pilot, the researcher identified one prison. At this prison, the researcher identified two different cellblocks, C-Block and D-Block. C-Block constitutes the treatment group, or the cellblock of inmates who will have their tobacco taken away. D-Block is the comparison group�inmates in this cellblock will retain their tobacco privileges during the course of the study and during a determined follow-up period to measure post-test assaults (e.g., 12-months). This is a two-group longitudinal design (also sometimes called a multiple interrupted time series design), and adding a comparison group makes this design superior to the one-group longitudinal design.

TABLE 5.6 | Two-Group Longitudinal Design

The usefulness of adding a comparison group to the study means that the researcher can have more confidence that the results at the post-test are due to the tobacco ban and not some alternative explanation. This is because any difference in assaults at the post-test between the treatment and comparison group should be attributed to the only difference between them, the tobacco ban. For this interpretation to hold, however, the researcher must be sure that C-Block and D-Block are similar or equivalent on all factors that might influence the post-test. There are many potential factors that should be considered. For example, the researcher will want to make sure that the same types of inmates are housed in both cellblocks. If a chronic group of assaultive inmates constitutes members of C-Block, but not D-Block, this differential could explain the results, not the treatment.

The researcher might also want to make sure equitable numbers of tobacco and non-tobacco users are found in each cellblock. If very few inmates in C-Block are smokers, the real effect of removing tobacco may be hidden. The researcher might also examine other areas where potential differences might arise, for example, that both cellblocks are staffed with equal numbers of officers, that officers in each cellblock tend to resolve inmate disputes similarly, and other potential issues that could influence post-test measure of assaults. Equivalence could also be ensured by comparing the groups on additional evidence before the ban takes effect: number of prior prison sentences, time served in prison, age, seriousness of conviction crime, and other factors that might relate to assaultive behavior, regardless of the tobacco ban. Moreover, the researcher should ensure that inmates in C-Block do not know that their D-Block counterparts are still allowed tobacco during the pilot study, and vice versa. If either group knows about the pilot program being an experiment, they might act differently than normal, and this could become an explanation of results. Additionally, the researchers might also try to make sure that C-Block inmates are completely tobacco free after the ban goes into effect�that they do not hoard, smuggle, or receive tobacco from officers or other inmates during the tobacco ban in or outside of the cellblock. If these and other important differences are accounted for at the individual and cellblock level, the researcher will have more confidence that any differences in assaults at the post-test between the treatment and comparison groups are related to the tobacco ban, and not some other difference between the two groups or the two cellblocks.

The addition of a comparison group aids in the ability of the researcher to isolate the true impact of a tobacco ban on inmate-on-inmate assaults. All factors that influence the treatment group should also influence the comparison group because the groups are made up of equivalent individuals in equivalent circumstances, with the exception of the tobacco ban. If this is the only difference, the results can be attributed to the ban. Although the addition of the comparison group in the two-group longitudinal design provides more confidence that the findings are attributed to the tobacco ban, the fact that this design lacks randomization means that alternative explanations cannot be completely ruled out�but they can be minimized. This example also suggests that the quasi-experiment in this instance may actually be preferable to an experimental design�noting the realities of prison administration. For example, prison inmates are not typically randomly assigned to different cellblocks by prison officers. Moreover, it is highly unlikely that a prison would have two open cellblocks waiting for a researcher to randomly assign incoming inmates to the prison for a tobacco ban study. Therefore, it is likely there would be differences among the groups in the quasi-experiment.

Fortunately, if differences between the groups are present, the researcher can attempt to determine their potential impact before interpretation of results. The researcher can also use statistical models after the ban takes effect to determine the impact of any differences between the groups on the post-test. While the two-group longitudinal quasi-experiment just discussed could also take the form of an experimental design, if random assignment could somehow be accomplished, the previous discussion provides one situation where an experimental design might be appropriate and desired for a particular research question, but would not be realistic considering the many barriers.

The Threat of Alternative Explanations

Alternative explanations are those factors that could explain the post-test results, other than the treatment. Throughout this chapter, we have noted the potential for alternative explanations and have given several examples of explanations other than the treatment. It is important to know that potential alternative explanations can arise in any research design discussed in this chapter. However, alternative explanations often arise because some design part is missing, for example, random assignment, a pre-test, or a control or comparison group. This is especially true in criminal justice where researchers often conduct field studies and have less control over their study conditions than do researchers who conduct experiments under highly controlled laboratory conditions. A prime example of this is the tobacco ban study, where it would be difficult for researchers to ensure that C-Block inmates, the treatment group, were completely tobacco free during the course of the study.

Alternative explanations are typically referred to as threats to internal validity. In this context, if an experiment is internally valid, it means that alternative explanations have been ruled out and the treatment is the only factor that produced the results. If a study is not internally valid, this means that alternative explanations for the results exist or potentially exist. In this section, we focus on some common alternative explanations that may arise in experimental and quasi-experimental designs. 27

Selection Bias

One of the more common alternative explanations that may occur is selection bias. Selection bias generally indicates that the treatment group (or experimental group) is somehow different from the comparison group (or control group) on a factor that could influence the post-test results. Selection bias is more often a threat in quasi-experimental designs than experimental designs due to the lack of random assignment. Suppose in our study of the prison tobacco ban, members of C-Block were substantially younger than members of D-Block, the comparison group. Such an imbalance between the groups would mean the researcher would not know if the differences in assaults are real (meaning the result of the tobacco ban) or a result of the age differential. Recall that research shows that younger inmates are more assaultive than older inmates and so we would expect more assaults among the younger offenders independent of the tobacco ban.

In a quasi-experiment, selection bias is perhaps the most prevalent type of alternative explanation and can seriously compromise results. Indeed, many of the examples above have referred to potential situations where the groups are imbalanced or not equivalent on some important factor. Although selection bias is a common threat in quasi-experimental designs because of lack of random assignment, and can be a threat in experimental designs because the groups could differ by chance alone or the practice of randomization was not maintained throughout the study (see Classics in CJ Research-MDVE above), a researcher may be able to detect such differentials. For example, the researcher could detect such differences by comparing the groups on the pre-test or other types of information before the start of the study. If differences were found, the researcher could take measures to correct them. The researcher could also use a statistical model that could account or control for differences between the groups and isolate the impact of the treatment, if any. This discussion is beyond the scope of this text but would be a potential way to deal with selection bias and estimate the impact of this bias on study results. The researcher could also, if possible, attempt to re-match the groups in a quasi-experiment or randomly assign the groups a second time in an experimental design to ensure equivalence. At the least, the researcher could recognize the group differences and discuss their potential impact on the results. Without a pre-test or other pre-study information on study participants, however, such differences might not be able to be detected and, therefore, it would be more difficult to determine how the differences, as a result of selection bias, influenced the results.

Another potential alternative explanation is history. History refers to any event experienced differently by the treatment and comparison groups in the time between the pre-test and the post-test that could impact results. Suppose during the course of the tobacco ban study several riots occurred on D-Block, the comparison group. Because of the riots, prison officers �locked down� this cellblock numerous times. Because D-Block inmates were locked down at various times, this could have affected their ability to otherwise engage in inmate assaults. At the end of the study, the assaults in D-Block might have decreased from their pre-test levels because of the lockdowns, whereas in C-Block assaults may have occurred at their normal pace because there was not a lockdown, or perhaps even increased from the pretest because tobacco was also taken away. Even if the tobacco ban had no effect and assaults remained constant in C-Block from pre- to post-test, the lockdown in D-Block might make it appear that the tobacco ban led to increased assaults in C-Block. Thus, the researcher would not know if the post-test results for the C-Block treatment group were attributable to the tobacco ban or the simple fact that D-Block inmates were locked down and their assault activity was artificially reduced. In this instance, the comparison group becomes much less useful because the lockdown created a historical factor that imbalanced the groups during the treatment phase and nullified the comparison.

Another potential alternative explanation is maturation. Maturation refers to the natural biological, psychological, or emotional processes we all experience as time passes�aging, becoming more or less intelligent, becoming bored, and so on. For example, if a researcher was interested in the effect of a boot camp on recidivism for juvenile offenders, it is possible that over the course of the boot camp program the delinquents naturally matured as they aged and this produced the reduction in recidivism�not that the boot camp somehow led to this reduction. This threat is particularly applicable in situations that deal with populations that rapidly change over a relatively short period of time or when a treatment lasts a considerable period of time. However, this threat could be eliminated with a comparison group that is similar to the treatment group. This is because the maturation effects would occur in both groups and the effect of the boot camp, if any, could be isolated. This assumes, however, that the groups are matched and equitable on factors subject to the maturation process, such as age. If not, such differentials could be an alternative explanation of results. For example, if the treatment and comparison groups differ by age, on average, this could mean that one group changes or matures at a different rate than the other group. This differential rate of change or maturation as a result of the age differential could explain the results, not the treatment. This example demonstrates how selection bias and maturation can interact at the same time as alternative explanations. This example also suggests the importance of an equivalent control or comparison group to eliminate or minimize the impact of maturation as an alternative explanation.

Attrition or Subject Mortality

Attrition or subject mortality is another typical alternative explanation. Attrition refers to differential loss in the number or type of subjects between the treatment and comparison groups and can occur in both experimental and quasi-experimental designs. Suppose we wanted to conduct a study to determine who is the better research methods professor among the authors of this textbook. Let�s assume that we have an experimental design where students were randomly assigned to professor 1, professor 2, or professor 3. By randomly assigning students to each respective professor, there is greater probability that the groups are equivalent and thus there are no differences between the three groups with one exception�the professor they receive and his or her particular teaching and delivery style. This is the treatment. Let�s also assume that the professors will be administering the same tests and using the same textbook. After the group members are randomly assigned, a pre-treatment evaluation shows the groups are in fact equivalent on all important known factors that could influence post-test scores, such as grade point average, age, time in school, and exposure to research methods concepts. Additionally, all groups scored comparably on a pre-test of knowledge about research methods, thus there is more confidence that the groups are in fact equivalent.

At the conclusion of the study, we find that professor 2�s group has the lowest final test scores of the three. However, because professor 2 is such an outstanding professor, the results appear odd. At first glance, the researcher thinks the results could have been influenced by students dropping out of the class. For example, perhaps several of professor 2�s students dropped the course but none did from the classes of professor 1 or 3. It is revealed, however, that an equal number of students dropped out of all three courses before the post-test and, therefore, this could not be the reason for the low scores in professor 2�s course. Upon further investigation, however, the researcher finds that although an equal number of students dropped out of each class, the dropouts in professor 2�s class were some of his best students. In contrast, those who dropped out of professor 1�s and professor 3�s courses were some of their poorest students. In this example, professor 2 appears to be the least effective teacher. However, this result appears to be due to the fact that his best students dropped out, and this highly influenced the final test average for his group. Although there was not a differential loss of subjects in terms of numbers (which can also be an attrition issue), there was differential loss in the types of students. This differential loss, not the teaching style, is an alternative explanation of the results.

Testing or Testing Bias

Another potential alternative explanation is testing or testing bias. Suppose that after the pre-test of research methods knowledge, professor 1 and professor 3 reviewed the test with their students and gave them the correct answers. Professor 2 did not. The fact that professor l�s and professor 3�s groups did better on the post-test final exam may be explained by the finding that students in those groups remembered the answers to the pre-test, were thus biased at the pre-test, and this artificially inflated their post-test scores. Testing bias can explain the results because students in groups 1 and 3 may have simply remembered the answers from the pre-test review. In fact, the students in professor l�s and 3�s courses may have scored high on the post-test without ever having been exposed to the treatment because they were biased at the pre-test.

Instrumentation

Another alternative explanation that can arise is instrumentation. Instrumentation refers to changes in the measuring instrument from pre- to post-test. Using the previous example, suppose professors 1 and 3 did not give the same final exam as professor 2. For example, professors 1 and 3 changed the final exam and professor 2 kept the final exam the same as the pretest. Because professors 1 and 3 changed the exam, and perhaps made it easier or somehow different from the pre-test exam, results that showed lower scores for professor 2�s students may be related only to instrumentation changes from pre- to post-test. Obviously, to limit the influence of instrumentation, researchers should make sure that instruments remain consistent from pre- to post-test.

A final alternative explanation is reactivity. Reactivity occurs when members of the treatment or experimental group change their behavior simply as a result of being part of a study. This is akin to the finding that people tend to change their behavior when they are being watched or are aware they are being studied. If members of the experiment know they are part of an experiment and are being studied and watched, it is possible that their behavior will change independent of the treatment. If this occurs, the researcher will not know if the behavior change is the result of the treatment, or simply a result of being part of a study. For example, suppose a researcher wants to determine if a boot camp program impacts the recidivism of delinquent offenders. Members of the experimental group are sentenced to boot camp and members of the control group are released on their own recognizance to their parents. Because members of the experimental group know they are part of the experiment, and hence being watched closely after they exit boot camp, they may artificially change their behavior and avoid trouble. Their change of behavior may be totally unrelated to boot camp, but rather, to their knowledge of being part of an experiment.

Other Potential Alternative Explanations

The above discussion provided some typical alternative explanations that may arise with the designs discussed in this chapter. There are, however, other potential alternative explanations that may arise. These alternative explanations arise only when a control or comparison group is present.

One such alternative explanation is diffusion of treatment. Diffusion of treatment occurs when the control or comparison group learns about the treatment its members are being denied and attempts to mimic the behavior of the treatment group. If the control group is successful in mimicking the experimental group, for example, the results at the end of the study may show similarity in outcomes between groups and cause the researcher to conclude that the program had no effect. In fact, however, the finding of no effect can be explained by the comparison group mimicking the treatment group. 28 In reality, there may be no effect of the treatment, but the researcher would not know this for sure because the control group effectively transformed into another experimental group�there is then no baseline of comparison. Consider a study where a researcher wants to determine the impact of a training program on class behavior and participation. In this study, the experimental group is exposed to several sessions of training on how to act appropriately in class and how to engage in class participation. The control group does not receive such training, but they are aware that they are part of an experiment. Suppose after a few class sessions the control group starts to mimic the behavior of the experimental group, acting the same way and participating in class the same way. At the conclusion of the study, the researcher might determine that the program had no impact because the comparison group, which did not receive the new program, showed similar progress.

In a related explanation, sometimes the comparison or control group learns about the experiment and attempts to compete with the experimental or treatment group. This alternative explanation is called compensatory rivalry. For example, suppose a police chief wants to determine if a new training program will increase the endurance of SWAT team officers. The chief randomly assigns SWAT members to either an experimental or control group. The experimental group will receive the new endurance training program and the control group will receive the normal program that has been used for years. During the course of the study, suppose the control group learns that the treatment group is receiving the new endurance program and starts to compete with the experimental group. Perhaps the control group runs five more miles per day and works out an extra hour in the weight room, in addition to their normal endurance program. At the end of the study, and due to the control group�s extra and competing effort, the results might show no effect of the new endurance program, and at worst, experimental group members may show a decline in endurance compared to the control group. The rivalry or competing behavior actually explains the results, not that the new endurance program has no effect or a damaging effect. Although the new endurance program may in reality have no effect, this cannot be known because of the actions of the control group, who learned about the treatment and competed with the experimental group.

Closely related to compensatory rivalry is the alternative explanation of comparison or control group demoralization. 29 In this instance, instead of competing with the experimental or treatment group, the control or comparison group simply gives up and changes their normal behavior. Using the SWAT example, perhaps the control group simply quits their normal endurance program when they learn about the treatment group receiving the new endurance program. At the post-test, their endurance will likely drop considerably compared to the treatment group. Because of this, the new endurance program might emerge as a shining success. In reality, however, the researcher will not know if any changes in endurance between the experimental and control groups are a result of the new endurance program or the control group giving up. Due to their giving up, there is no longer a comparison group of equitable others, the change in endurance among the treatment group members could be attributed to a number of alternative explanations, for example, maturation. If the comparison group behaves normally, the researcher will be able to exclude maturation as a potential explanation. This is because any maturation effects will occur in both groups.

The previous discussion suggests that when the control or comparison group learns about the experiment and the treatment they are denied, potential alternative explanations can arise. Perhaps the best remedy to protect from the alternative explanations just discussed is to make sure the treatment and comparison groups do not have contact with one another. In laboratory experiments this can be ensured, but sometimes this is a problem in criminal justice studies, which are often conducted in the field.

The previous discussion also suggests that there are numerous alternative explanations that can impact the interpretation of results from a study. A careful researcher would know that alternative explanations must be ruled out before reaching a definitive conclusion about the impact of a particular program. The researcher must be attuned to these potential alternative explanations because they can influence results and how results are interpreted. Moreover, the discussion shows that several alternative explanations can occur at the same time. For example, it is possible that selection bias, maturation, attrition, and compensatory rivalry all emerge as alternative explanations in the same study. Knowing about these potential alternative explanations and how they can impact the results of a study is what distinguishes a consumer of research from an educated consumer of research.

Chapter Summary

The primary focus of this chapter was the classic experimental design, the foundation for other types of experimental and quasi-experimental designs. The classic experimental design is perhaps the most useful design when exploring causal relationships. Often, however, researchers cannot employ the classic experimental design to answer a research question. In fact, the classic experimental design is rare in criminal justice and criminology because it is often difficult to ensure random assignment for a variety of reasons. In circumstances where an experimental design is appropriate but not feasible, researchers may turn to one of many quasi-experimental designs. The most important difference between the two is that quasi-experimental designs do not feature random assignment. This can create potential problems for researchers. The main problem is that there is a greater chance the treatment and comparison groups may differ on important characteristics that could influence the results of a study. Although researchers can attempt to prevent imbalances between the groups by matching them on important known characteristics, it is still much more difficult to establish equivalence than it is in the classic experiment. As such, it becomes more difficult to determine what impact a treatment had, if any, as one moves from an experimental to a quasi-experimental design.

Perhaps the most important lesson to be learned in this chapter is that to be an educated consumer of research results requires an understanding of the type of design that produced the results. There are numerous ways experimental and quasi-experimental designs can be structured. This is why much attention was paid to the classic experimental design. In reality, all experimental and quasi-experimental designs are variations of the classic experiment in some way�adding or deleting certain components. If the components and organization and logic of the classic experimental design are understood, consumers of research will have a better understanding of the results produced from any sort of research design. For example, what problems in interpretation arise when a design lacks a pre-test, a control group, or random assignment? Having an answer to this question is a good start toward being an informed consumer of research results produced through experimental and quasi-experimental designs.

Critical Thinking Questions

1. Why is randomization/random assignment preferable to matching? Provide several reasons with explanation.

2. What are some potential reasons a researcher would not be able to utilize random assignment?

3. What is a major limitation of matching?

4. What is the difference between a longitudinal study and a cross-sectional study?

5. Describe a hypothetical study where maturation, and not the treatment, could explain the outcomes of the research.

association (or covariance or correlation): One of three conditions that must be met for establishing cause and effect, or a causal relationship. Association refers to the condition that X and Y must be related for a causal relationship to exist. Association is also referred to as covariance or correlation. Although two variables may be associated (or covary or be correlated), this does not automatically imply that they are causally related

attrition or subject mortality: A threat to internal validity, it refers to the differential loss of subjects between the experimental (treatment) and control (comparison) groups during the course of a study

cause and effect relationship: A cause and effect relationship occurs when one variable causes another, and no other explanation for that relationship exists

classic experimental design or experimental design: A design in a research study that features random assignment to an experimental or control group. Experimental designs can vary tremendously, but a constant feature is random assignment, experimental and control groups, and a post-test. For example, a classic experimental design features random assignment, a treatment, experimental and control groups, and pre- and post-tests

comparison group: The group in a quasi-experimental design that does not receive the treatment. In an experimental design, the comparison group is referred to as the control group

compensatory rivalry: A threat to internal validity, it occurs when the control or comparison group attempts to compete with the experimental or treatment group

control group: In an experimental design, the control group does not receive the treatment. The control group serves as a baseline of comparison to the experimental group. It serves as an example of what happens when a group equivalent to the experimental group does not receive the treatment

cross-sectional designs: A measurement of the pre-test and post-test at one point in time (e.g., six months before and six months after the program)

demoralization: A threat to internal validity closely associated with compensatory rivalry, it occurs when the control or comparison group gives up and changes their normal behavior. While in compensatory rivalry the group members compete, in demoralization, they simply quit. Both are not normal behavioral reactions

dependent variable: Also known as the outcome in a research study. A post-test is a measure of the dependent variable

diffusion of treatment: A threat to internal validity, it occurs when the control or comparison group members learn that they are not getting the treatment and attempt to mimic the behavior of the experimental or treatment group. This mimicking may make it seem as if the treatment is having no effect, when in fact it may be

elimination of alternative explanations: One of three conditions that must be met for establishing cause and effect. Elimination of alternative explanations means that the researcher has ruled out other explanations for an observed relationship between X and Y

experimental group: In an experimental design, the experimental group receives the treatment

history: A threat to internal validity, it refers to any event experienced differently by the treatment and comparison groups�an event that could explain the results other than the supposed cause

independent variable: Also called the cause

instrumentation: A threat to internal validity, it refers to changes in the measuring instrument from pre- to post-test

longitudinal: Refers to repeated measurements of the pre-test and post-test over time, typically for the same group of individuals. This is the opposite of cross-sectional

matching: A process sometimes utilized in some quasi-experimental designs that feature treatment and comparison groups. Matching is a process whereby the researcher attempts to ensure equivalence between the treatment and comparison groups on known information, in the absence of the ability to randomly assign the groups

maturation: A threat to internal validity, maturation refers to the natural biological, psychological, or emotional processes as time passes

negative association: Refers to a negative association between two variables. A negative association is demonstrated when X increases and Y decreases, or X decreases and Y increases. Also known as an inverse relationship�the variables moving in opposite directions

operationalized or operationalization: Refers to the process of assigning a working definition to a concept. For example, the concept of intelligence can be operationalized or defined as grade point average or score on a standardized exam, among others

pilot program or test: Refers to a smaller test study or pilot to work out problems before a larger study and to anticipate changes needed for a larger study. Similar to a test run

positive association: Refers to a positive association between two variables. A positive association means as X increases, Y increases, or as X decreases, Y decreases

post-test: The post-test is a measure of the dependent variable after the treatment has been administered

pre-test: The pre-test is a measure of the dependent variable or outcome before a treatment is administered

quasi-experiment: A quasi-experiment refers to any number of research design configurations that resemble an experimental design but primarily lack random assignment. In the absence of random assignment, quasi-experimental designs feature matching to attempt equivalence

random assignment: Refers to a process whereby members of the experimental group and control group are assigned to each group through a random and unbiased process

random selection: Refers to selecting a smaller but representative subset from a population. Not to be confused with random assignment

reactivity: A threat to internal validity, it occurs when members of the experimental (treatment) or control (comparison) group change their behavior unnaturally as a result of being part of a study

selection bias: A threat to internal validity, selection bias occurs when the experimental (treatment) group and control (comparison) group are not equivalent. The difference between the groups can be a threat to internal validity, or, an alternative explanation to the findings

spurious: A spurious relationship is one where X and Y appear to be causally related, but in fact the relationship is actually explained by a variable or factor other than X

testing or testing bias: A threat to internal validity, it refers to the potential of study members being biased prior to a treatment, and this bias, rather than the treatment, may explain study results

threat to internal validity: Also known as alternative explanation to a relationship between X and Y. Threats to internal validity are factors that explain Y, or the dependent variable, and are not X, or the independent variable

timing: One of three conditions that must be met for establishing cause and effect. Timing refers to the condition that X must come before Y in time for X to be a cause of Y. While timing is necessary for a causal relationship, it is not sufficient, and considerations of association and eliminating other alternative explanations must be met

treatment: A component of a research design, it is typically denoted by the letter X. In a research study on the impact of teen court on juvenile recidivism, teen court is the treatment. In a classic experimental design, the treatment is given only to the experimental group, not the control group

treatment group: The group in a quasi-experimental design that receives the treatment. In an experimental design, this group is called the experimental group

unit of analysis: Refers to the focus of a research study as being individuals, groups, or other units of analysis, such as prisons or police agencies, and so on

variable(s): A variable is a concept that has been given a working definition and can take on different values. For example, intelligence can be defined as a person�s grade point average and can range from low to high or can be defined numerically by different values such as 3.5 or 4.0

1 Povitsky, W., N. Connell, D. Wilson, & D. Gottfredson. (2008). �An experimental evaluation of teen courts.� Journal of Experimental Criminology, 4, 137�163.

2 Hirschi, T., and H. Selvin (1966). �False criteria of causality in delinquency.� Social Problems, 13, 254�268.

3 Robert Roy Britt, �Churchgoers Live Longer.� April, 3, 2006. http://www.livescience.com/health/060403_church_ good.html. Retrieved on September 30, 2008.

4 Kalist, D., and D. Yee (2009). �First names and crime: Does unpopularity spell trouble?� Social Science Quarterly, 90 (1), 39�48.

5 Sherman, L. (1992). Policing domestic violence. New York: The Free Press.

6 For historical and interesting reading on the effects of weather on crime and other disorder, see Dexter, E. (1899). �Influence of weather upon crime.� Popular Science Monthly, 55, 653�660 in Horton, D. (2000). Pioneering Perspectives in Criminology. Incline Village, NV: Copperhouse.

7 http://www.escapistmagazine.com/news/view/111191-Less-Crime-in-U-S-Thanks-to-Videogames , retrieved on September 13, 2011. This news article was in response to a study titled �Understanding the effects of violent videogames on violent crime.� See Cunningham, Scott, Engelst�tter, Benjamin, and Ward, (April 7, 2011). Available at SSRN: http://ssm.com/abstract= 1804959.

8 Cohn, E. G. (1987). �Changing the domestic violence policies of urban police departments: Impact of the Minneapolis experiment.� Response, 10 (4), 22�24.

9 Schmidt, Janell D., & Lawrence W. Sherman (1993). �Does arrest deter domestic violence?� American Behavioral Scientist, 36 (5), 601�610.

10 Maxwell, Christopher D., Joel H. Gamer, & Jeffrey A. Fagan. (2001). The effects of arrest on intimate partner violence: New evidence for the spouse assault replication program. Washington D.C.: National Institute of Justice.

11 Miller, N. (2005). What does research and evaluation say about domestic violence laws? A compendium of justice system laws and related research assessments. Alexandria, VA: Institute for Law and Justice.

12 The sections on experimental and quasi-experimental designs rely heavily on the seminal work of Campbell and Stanley (Campbell, D.T., & J. C. Stanley. (1963). Experimental and quasi-experimental designs for research. Chicago: RandMcNally) and more recently, Shadish, W., T. Cook, & D. Campbell. (2002). Experimental and quasi-experimental designs for generalized causal inference. New York: Houghton Mifflin.

13 Povitsky et al. (2008). p. 146, note 9.

14 Shadish, W., T. Cook, & D. Campbell. (2002). Experimental and quasi-experimental designs for generalized causal inference. New York: Houghton Mifflin Company.

15 Ibid, 15.

16 Finckenauer, James O. (1982). Scared straight! and the panacea phenomenon. Englewood Cliffs, N.J.: Prentice Hall.

17 Yarborough, J.C. (1979). Evaluation of JOLT (Juvenile Offenders Learn Truth) as a deterrence program. Lansing, MI: Michigan Department of Corrections.

18 Petrosino, Anthony, Carolyn Turpin-Petrosino, & James O. Finckenauer. (2000). �Well-meaning programs can have harmful effects! Lessons from experiments of programs such as Scared Straight.� Crime and Delinquency, 46, 354�379.

19 �Swearing makes pain more tolerable� retrieved at http:// www.livescience.com/health/090712-swearing-pain.html (July 13, 2009). Also see �Bleep! My finger! Why swearing helps ease pain� by Tiffany Sharpies, retrieved at http://www.time.com/time/health/article /0,8599,1910691,00.html?xid=rss-health (July 16, 2009).

20 For an excellent discussion of the value of controlled experiments and why they are so rare in the social sciences, see Sherman, L. (1992). Policing domestic violence. New York: The Free Press, 55�74.

21 For discussion, see Weisburd, D., T. Einat, & M. Kowalski. (2008). �The miracle of the cells: An experimental study of interventions to increase payment of court-ordered financial obligations.� Criminology and Public Policy, 7, 9�36.

22 Shadish, Cook, & Campbell. (2002).

24 Kelly, Cathy. (March 15, 2009). �Tickets in the mail: Red-light cameras questioned.� Santa Cruz Sentinel.

25 Retting, Richard, Susan Ferguson, & Charles Farmer. (January 2007). �Reducing red light running through longer yellow signal timing and red light camera enforcement: Results of a field investigation.� Arlington, VA: Insurance Institute for Highway Safety.

26 Shadish, Cook, & Campbell. (2002).

27 See Shadish, Cook, & Campbell. (2002), pp. 54�61 for an excellent discussion of threats to internal validity. Also see Chapter 2 for an extended discussion of all forms of validity considered in research design.

28 Trochim, W. (2001). The research methods knowledge base, 2nd ed. Cincinnati, OH: Atomic Dog.

Applied Research Methods in Criminal Justice and Criminology by University of North Texas is licensed under a Creative Commons Attribution-NonCommercial 4.0 International License , except where otherwise noted.

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Quasi-Experimental Designs for Causal Inference

When randomized experiments are infeasible, quasi-experimental designs can be exploited to evaluate causal treatment effects. The strongest quasi-experimental designs for causal inference are regression discontinuity designs, instrumental variable designs, matching and propensity score designs, and comparative interrupted time series designs. This article introduces for each design the basic rationale, discusses the assumptions required for identifying a causal effect, outlines methods for estimating the effect, and highlights potential validity threats and strategies for dealing with them. Causal estimands and identification results are formalized with the potential outcomes notations of the Rubin causal model.

Causal inference plays a central role in many social and behavioral sciences, including psychology and education. But drawing valid causal conclusions is challenging because they are warranted only if the study design meets a set of strong and frequently untestable assumptions. Thus, studies aiming at causal inference should employ designs and design elements that are able to rule out most plausible threats to validity. Randomized controlled trials (RCTs) are considered as the gold standard for causal inference because they rely on the fewest and weakest assumptions. But under certain conditions quasi-experimental designs that lack random assignment can also be as credible as RCTs ( Shadish, Cook, & Campbell, 2002 ).

This article discusses four of the strongest quasi-experimental designs for identifying causal effects: regression discontinuity design, instrumental variable design, matching and propensity score designs, and the comparative interrupted time series design. For each design we outline the strategy and assumptions for identifying a causal effect, address estimation methods, and discuss practical issues and suggestions for strengthening the basic designs. To highlight the design differences, throughout the article we use a hypothetical example with the following causal research question: What is the effect of attending a summer science camp on students’ science achievement?

POTENTIAL OUTCOMES AND RANDOMIZED CONTROLLED TRIAL

Before we discuss the four quasi-experimental designs, we introduce the potential outcomes notation of the Rubin causal model (RCM) and show how it is used in the context of an RCT. The RCM ( Holland, 1986 ) formalizes causal inference in terms of potential outcomes, which allow us to precisely define causal quantities of interest and to explicate the assumptions required for identifying them. RCM considers a potential outcome for each possible treatment condition. For a dichotomous treatment variable (i.e., a treatment and control condition), each subject i has a potential treatment outcome Y i (1), which we would observe if subject i receives the treatment ( Z i = 1), and a potential control outcome Y i (0), which we would observe if subject i receives the control condition ( Z i = 0). The difference in the two potential outcomes, Y i (1)− Y i (0), represents the individual causal effect.

Suppose we want to evaluate the effect of attending a summer science camp on students’ science achievement score. Then each student has two potential outcomes: a potential control score for not attending the science camp, and the potential treatment score for attending the camp. However, the individual causal effects of attending the camp cannot be inferred from data, because the two potential outcomes are never observed simultaneously. Instead, researchers typically focus on average causal effects. The average treatment effect (ATE) for the entire study population is defined as the difference in the expected potential outcomes, ATE = E [ Y i (1)] − E [ Y i (0)]. Similarly, we can also define the ATE for the treated subjects (ATT), ATT = E [ Y i (1) | Z i = 1] − E [ Y (0) | Z i =1]. Although the expectations of the potential outcomes are not directly observable because not all potential outcomes are observed, we nonetheless can identify ATE or ATT under some reasonable assumptions. In an RCT, random assignment establishes independence between the potential outcomes and the treatment status, which allows us to infer ATE. Suppose that students are randomly assigned to the science camp and that all students comply with the assigned condition. Then random assignment guarantees that the camp attendance indicator Z is independent of the potential achievement scores Y i (0) and Y i (1).

The independence assumption allows us to rewrite ATE in terms of observable expectations (i.e., with observed outcomes instead of potential outcomes). First, due to the independence (randomization), the unconditional expectations of the potential outcomes can be expressed as conditional expectations, E [ Y i (1)] = E [ Y i (1) | Z i = 1] and E [ Y i (0)] = E [ Y i (0) | Z i = 0] Second, because the potential treatment outcomes are actually observed for the treated, we can replace the potential treatment outcome with the observed outcome such that E [ Y i (1) | Z i = 1] = E [ Y i | Z i = 1] and, analogously, E [ Y i (0) | Z i = 0] = E [ Y i | Z i = 0] Thus, the ATE is expressible in terms of observable quantities rather than potential outcomes, ATE = E [ Y i (1)] − E [ Y i (0)] = E [ Y i | Z i = 1] – E [ Y i | Z i = 0], and we that say ATE is identified.

This derivation also rests on the stable-unit-treatment-value assumption (SUTVA; Imbens & Rubin, 2015 ). SUTVA is required to properly define the potential outcomes, that is, (a) the potential outcomes of a subject depend neither on the assignment mode nor on other subjects’ treatment assignment, and (b) there is only one unique treatment and one unique control condition. Without further mentioning, we assume SUTVA for all quasi-experimental designs discussed in this article.

REGRESSION DISCONTINUITY DESIGN

Due to ethical or budgetary reasons, random assignment is often infeasible in practice. Nonetheless, researchers may sometimes still retain full control over treatment assignment as in a regression discontinuity (RD) design where, based on a continuous assignment variable and a cutoff score, subjects are deterministically assigned to treatment conditions.

Suppose that the science camp is a remedial program and only students whose grade point average (GPA) score is less than or equal to 2.0 are eligible to participate. Figure 1 shows a scatterplot of hypothetical data where the x-axis represents the assignment variable ( GPA ) and the y -axis the outcome ( Science Score ). All subjects with a GPA score below the cutoff attended the camp (circles), whereas all subjects scoring above the cutoff do not attend (squares). Because all low-achieving students are in the treatment group and all high-achieving students in the control group, their respective GPA distributions do not overlap, not even at the cutoff. This lack of overlap complicates the identification of a causal effect because students in the treatment and control group are not comparable at all (i.e., they have a completely different distribution of the GPA scores).

A hypothetical example of regression discontinuity design. Note . GPA = grade point average.

One strategy of dealing with the lack of overlap is to rely on the linearity assumption of regression models and to extrapolate into areas of nonoverlap. However, if the linear models do not correctly specify the functional form, the resulting ATE estimate is biased. A safer strategy is to evaluate the treatment effect only at the cutoff score where treatment and control cases almost overlap, and thus functional form assumptions and extrapolation are almost no longer needed. Consider the treatment and control students that score right at the cutoff or just above it. Students with a GPA score of 2.0 participate in the science camp and students with a GPA score of 2.1 are in the control condition (the status quo condition or a different camp). The two groups of students are essentially equivalent because the difference in their GPA scores is negligibly small (2.1 − 2.0 = .1) and likely due to random chance (measurement error) rather than a real difference in ability. Thus, in the very close neighborhood around the cutoff score, the RD design is equivalent to an RCT; therefore, the ATE at the cutoff (ATEC) is identified.

CAUSAL ESTIMAND AND IDENTIFICATION

ATEC is defined as the difference in the expected potential treatment and control outcomes for the subjects scoring exactly at the cutoff: ATEC = E [ Y i (1) | A i = a c ] − E [ Y i (0) | A i = a c ], where A denotes assignment variable and a c the cutoff score. Because we observe only treatment subjects and not control subjects right at the cutoff, we need two assumptions in order to identify ATEC ( Hahn, Todd, & van Klaauw, 2001 ): (a) the conditional expectations of the potential treatment and control outcomes are continuous at the cutoff ( continuity ), and (b) all subjects comply with treatment assignment ( full compliance ).

The continuity assumption can be expressed in terms of limits as lim a ↓ a C E [ Y i ( 1 ) | A i = a ] = E [ Y i ( 1 ) | A i = a ] = lim a ↑ a C E [ Y i ( 1 ) | A i = a ] and lim a ↓ a C E [ Y i ( 0 ) | A i = a ] = E [ Y i ( 0 ) | A i = a ] = lim a ↑ a C E [ Y i ( 0 ) | A i = a ] . Thus, we can rewrite ATEC as the difference in limits, A T E C = lim a ↑ a C E [ Y i ( 1 ) | A i = a c ] − lim a ↓ a C E [ Y i ( 0 ) | A i = a c ] , which solves the issue that no control subjects are observed directly at the cutoff. Then, by the full compliance assumption, the potential treatment and control outcomes can be replaced with the observed outcomes such that A T E C = lim a ↑ a C E [ Y i | A i = a c ] − lim a ↓ a C E [ Y i | A i = a c ] is identified at the cutoff (i.e., ATEC is now expressed in terms of observable quantities). The difference in the limits represents the discontinuity in the mean outcomes exactly at the cutoff ( Figure 1 ).

Estimating ATEC

ATEC can be estimated with parametric or nonparametric regression methods. First, consider the parametric regression of the outcome Y on the treatment Z , the cutoff-centered assignment variable A − a c , and their interaction: Y = β 0 + β 1 Z + β 2 ( A − a c ) + β 3 ( Z × ( A − a c )) + e . If the model correctly specifies the functional form, then β ^ 1 is an unbiased estimator for ATEC. In practice, an appropriate model specification frequently involves also quadratic and cubic terms of the assignment variable plus their interactions with the treatment indicator.

To avoid overly strong functional form assumptions, semiparametric or nonparametric regression methods like generalized additive models or local linear kernel regression can be employed ( Imbens & Lemieux, 2008 ). These methods down-weight or even discard observations that are not in the close neighborhood around the cutoff. The R packages rdd ( Dimmery, 2013 ) and rdrobust ( Calonico, Cattaneo, & Titiunik, 2015 ), or the command rd in STATA ( Nichols, 2007 ) are useful for estimation and diagnostic purposes.

Practical Issues

A major validity threat for RD designs is the manipulation of the assignment score around the cutoff, which directly results in a violation of the continuity assumption ( Wong et al., 2012 ). For instance, if a teacher knows the assignment score in advance and he wants all his students to attend the science camp, the teacher could falsely report a GPA score of 2.0 or below for the students whose actual GPA score exceeds the cutoff value.

Another validity threat is noncompliance, meaning that subjects assigned to the control condition may cross over to the treatment and subjects assigned to the treatment do not show up. An RD design with noncompliance is called a fuzzy RD design (instead of a sharp RD design with full compliance). A fuzzy RD design still allows us to identify the intention-to-treat effect or the local average treatment effect at the cutoff (LATEC). The intention-to-treat effect refers to the effect of treatment assignment rather than the actual treatment receipt. LATEC estimates ATEC for the subjects who comply with treatment assignment. LATEC is identified if one uses the assignment status as an instrumental variable for treatment receipt (see the upcoming Instrumental Variable section).

Finally, generalizability and statistical power are often mentioned as major disadvantages of RD designs. Because RD designs identify the treatment effect only at the cutoff, ATEC estimates are not automatically generalizable to subjects scoring further away from the cutoff. Statistical power for detecting a significant effect is an issue because the lack of overlap on the assignment variable results in increased standard errors. With semi- or nonparametric regression methods, power further diminishes.

Strengthening RD Designs

To avoid systematic manipulations of the assignment variable, it is desirable to conceal the assignment rule from study participants and administrators. If the assignment rule is known to them, manipulations can hardly be ruled out, particularly when the stakes are high. Researchers can use the McCrary test ( McCrary, 2008 ) to check for potential manipulations. The test investigates whether there is a discontinuity in the distribution of the assignment variable right at the cutoff. Plotting baseline covariates against the assignment variable, and regressing the covariates on the assignment variable and the treatment indicator also help in detecting potential discontinuities at the cutoff.

The RD design’s validity can be increased by combining the basic RD design with other designs. An example is the tie-breaking RD design, which uses two cutoff scores. Subjects scoring between the two cutoff scores are randomly assigned to treatment conditions, whereas subjects scoring outside the cutoff interval receive the treatment or control condition according to the RD assignment rule ( Black, Galdo & Smith, 2007 ). This design combines an RD design with an RCT and is advantageous with respect to the correct specification of the functional form, generalizability, and statistical power. Similar benefits can be obtained by adding pretest measures of the outcome or nonequivalent comparison groups ( Wing & Cook, 2013 ).

Imbens and Lemieux (2008) and Lee and Lemieux (2010) provided comprehensive introductions to RD designs. Lee and Lemieux also summarized many applications from economics. Angrist and Lavy (1999) applied the design to investigate the effect of class size on student achievement.

INSTRUMENTAL VARIABLE DESIGN

In practice, researchers often have no or only partial control over treatment selection. In addition, they might also lack reliable knowledge of the selection process. Nonetheless, even with limited control and knowledge of the selection process it is still possible to identify a causal treatment effect if an instrumental variable (IV) is available. An IV is an exogenous variable that is related to the treatment but is completely unrelated to the outcome, except via treatment. An IV design requires researchers either to create an IV at the design stage (as in an encouragement design; see next) or to find an IV in the data set at hand or a related data base.

Consider the science camp example, but instead of random or deterministic treatment assignment, students decide on their own or together with their parents whether to attend the camp. Many factors may determine the decision, for instance, students’ science ability and motivation, parents’ socioeconomic status, or the availability of public transportation for the daily commute to the camp. Whereas the first three variables are presumably also related to the science outcome, public transportation might be unrelated to the science score (except via camp attendance). Thus, the availability of public transportation may qualify as an IV. Figure 2 illustrates such IV design: Public transportation (IV) directly affects camp attendance but has no direct or indirect effect on science achievement (outcome) other than through camp attendance (treatment). The question mark represents unknown or unobserved confounders, that is, variables that simultaneously affect both camp attendance and science achievement. The IV design allows us to identify a causal effect even if some or all confounders are unknown or unobserved.

A diagram of an example of instrumental variable design.

The strategy for identifying a causal effect is based on exploiting the variation in the treatment variable explained by IV. In Figure 2 , the total variation in the treatment consists of (a) the variation induced by the IV and (b) the variation induced by confounders (question mark) and other exogenous variables (not shown in the figure). The identification of the camp’s effect requires us to isolate the treatment variation that is related to public transportation (IV), and then to use the isolated variation to investigate the camp’s effect on the science score. Because we exploit the treatment variation exclusively induced by the IV but ignore the variation induced by unobserved or unknown confounders, the IV design identifies the ATE for the sub-population of compliers only. In our example, the compliers are the students who attend the camp because public transportation is available and do not attend because it is unavailable. For students whose parents always use their own car to drop them off and pick them up at the camp location, we cannot infer the causal effect, because their camp attendance is completely unrelated to the availability of public transportation.

Causal Estimand and Identification

The complier average treatment effect (CATE) is defined as the expected difference in potential outcomes for the sub-population of compliers: CATE = E [ Y i (1) | Complier ] − E [ Y i (0) | Complier ] = τ C .

Identification requires us to distinguish between four latent groups: compliers (C), who attend the camp if public transportation is available but do not attend if unavailable; always-takers (A), who always attend the camp regardless of whether or not public transportation is available; never-takers (N), who never attend the camp regardless of public transportation; and defiers (D), who do not attend if public transportation is available but attend if unavailable. Because group membership is unknown, it is impossible to directly infer CATE from the data of compliers. However, CATE is identified from the entire data set if (a) the IV is predictive of the treatment ( predictive first stage ), (b) the IV is unrelated to the outcome except via treatment ( exclusion restriction ), and (c) no defiers are present ( monotonicity ; Angrist, Imbens, & Rubin, 1996 ; see Steiner, Kim, Hall, & Su, 2015 , for a graphical explanation).

First, notice that the IV’s effects on the treatment (γ) and the outcome (δ) are directly identified from the observed data because the IV’s relation with the treatment and outcome is unconfounded. In our example ( Figure 2 ), γ denotes the effect of public transportation on camp attendance and δ the indirect effect of public transportation on the science score. Both effects can be written as weighted averages of the corresponding group-specific effects ( γ C , γ A , γ N , γ D and δ C , δ A , δ N , δ D for compliers, always-takers, never-takers, and defiers, respectively): γ = p ( C ) γ C + p ( A ) γA + p ( N ) γ N + p ( D ) γ D and δ = p ( C ) δ C + p ( A ) δ A + p ( N ) δ N + p ( D ) δ D where p (.) represents the portion of the respective latent group in the population and p ( C ) + p ( A ) + p ( N ) + p ( D ) = 1. Because the treatment choice of always-takers and never-takers is entirely unaffected by the instrument, the IV’s effect on the treatment is zero, γ A = γ N = .0, and together with the exclusion restriction , we also know δ A = δ N = 0, that is, the IV has no effect on the outcome. If no defiers are present, p ( D ) = 0 ( monotonicity ), then the IV’s effects on the treatment and outcome simplify to γ = p ( C ) γC and δ = p ( C ) δC , respectively. Because δ C = γ C τ C and γ ≠ 0 ( predictive first stage ), the ratio of the observable IV effects, γ and δ, identifies CATE: δ γ = p ( C ) γ C τ C p ( C ) γ C = τ C .

Estimating CATE

A two-stage least squares (2SLS) regression is typically used for estimating CATE. In the first stage, treatment Z is regressed on the IV, Z = β 0 + β 1 IV + e . The linear first-stage model applies with a dichotomous treatment variable (linear probability model). The second stage then regresses the outcome Y on the predicted values Z ^ from the first stage model, Y = π 0 + π 1 Z ^ + r , where π ^ 1 is the CATE estimator. The two stages are automatically performed by the 2SLS procedure, which also provides an appropriate standard error for the effect estimate. The STATA commands ivregress and ivreg2 ( Baum, Schaffer, & Stillman, 2007 ) or the sem package in R ( Fox, 2006 ) perform the 2SLS regression.

One challenge in implementing an IV design is to find a valid instrument that satisfies the assumptions just discussed. In particular, the exclusion restriction is untestable and frequently hard to defend in practice. In our example, if high-income families live in suburban areas with bad public transportation connections, then the availability of the public transportation is likely related to the science score via household income (or socioeconomic status). Although conditioning on the observed household income can transform public transportation into a conditional IV (see next), one can frequently come up with additional scenarios that explains why the IV is related to the outcome and thus violates the exclusion restriction.

Another issue arises from “weak” IVs that are only weakly related to treatment. Weak IVs cause efficiency problems ( Wooldridge, 2012 ). If the availability of public transportation barely affects camp attendance because most parents give their children a ride anyway, the IV’s effect on the treatment ( γ ) is close to zero. Because γ ^ is the denominator in the CATE estimator, τ ^ C = δ ^ / γ ^ , an imprecisely estimated γ ^ results in a considerable over- or underestimation of CATE. Moreover, standard errors will be large.

One also needs to keep in mind that the substantive meaning of CATE depends on the chosen IV. Consider two slightly different IVs with respect to public transportation: the availability of (a) a bus service and (b) subway service. For the first IV, the complier population consists of students who choose to (not) attend the camp depending on the availability of a bus service. For the second IV, the complier population refers to the availability of a subway service. Because the two complier populations are very likely different from each other (students who are willing to take the subway might not be willing to take the bus), the corresponding CATEs refer to different subpopulations.

Strengthening IV Designs

Given the challenges in identifying a valid instrument from observed data, researchers should consider creating an IV at the design stage of a study. Although it might be impossible to directly assign subjects to treatment conditions, one might still be able to encourage participants to take the treatment. Subjects are randomly encouraged to sign up for treatment, but whether they actually comply with the encouragement is entirely their own decision ( Imai et al., 2011 ). Random encouragement qualifies as an IV because it very likely meets the exclusion restriction. For example, instead of collecting data on public transportation, researchers may advertise and recommend the science camp in a letter to the parents of a randomly selected sample of students.

With observational data it is hard to identify a valid IV because covariates that strongly predict the treatment are usually also related to the outcome. However, these covariates can still qualify as an IV if they affect the outcome only indirectly via other observed variables. Such covariates can be used as conditional IVs, that is, they meet the IV requirements conditional on the observed variables ( Brito & Pearl, 2002 ). Assume the availability of public transportation (IV) is associated with the science score via household income. Then, controlling for the reliably measured household income in both stages of the 2SLS analysis blocks the IV’s relation to the science score and turns public transportation into a conditional IV. However, controlling for a large set of variables does not guarantee that the exclusion restriction is more likely met. It may even result in more bias as compared to an IV analysis with fewer covariates ( Ding & Miratrix, 2015 ; Steiner & Kim, in press ). The choice of a valid conditional IV requires researchers to carefully select the control variables based on subject-matter theory.

The seminal article by Angrist et al. (1996) provides a thorough discussion of the IV design, and Steiner, Kim, et al. (2015 ) proved the identification result using graphical models. Excellent introductions to IV designs can be found in Angrist and Pischke (2009 , 2015) . Angrist and Krueger (1992) is an example of a creative application of the design with birthday as the IV. For encouragement designs, see Holland (1988) and Imai et al. (2011) .

MATCHING AND PROPENSITY SCORE DESIGN

This section considers quasi-experimental designs in which researchers lack control over treatment selection but have good knowledge about the selection mechanism or at least the confounders that simultaneously determine the treatment selection and the outcome. Due to self or third-person selection of subjects into treatment, the resulting treatment and control groups typically differ in observed but also unobserved baseline covariates. If we have reliable measures of all confounding covariates, then matching or propensity score (PS) designs balance groups on observed baseline covariates and thus enable the identification of causal effects ( Imbens & Rubin, 2015 ). Regression analysis and the analysis of covariance can also remove the confounding bias, but because they rely on functional form assumptions and extrapolation we discuss only nonparametric matching and PS designs.

Suppose that students decide on their own whether to attend the science camp. Although many factors can affect students’ decision, teachers with several years of experience of running the camp may know that selection is mostly driven by students’ science ability, liking of science, and their parents’ socioeconomic status. If all the selection-relevant factors that also affect the outcome are known, the question mark in Figure 2 can be replaced by the known confounding covariates.

Given the set of confounding covariates, causal inference with matching or PS designs is straightforward, at least theoretically. The basic one-to-one matching design matches each treatment subject to a control subject that is equivalent or at least very similar in observed covariates. To illustrate the idea of matching, consider a camp attendee with baseline measures of 80 on the science pre-test, 6 on liking science, and 50 on the socioeconomic status. Then a multivariate matching strategy tries to find a nonattendee with exactly the same or at least very similar baseline measures. If we succeed in finding close matches for all camp attendee, the matched samples of attendees and nonattendees will have almost identical covariate distributions.

Although multivariate matching works well when the number of confounders is small and the pool of control subjects is large relative to the number of treatment subjects, it is usually difficult to find close matches with a large set of covariates or a small pool of control subjects. Matching on the PS helps to overcome this issue because the PS is a univariate score computed from the observed covariates ( Rosenbaum & Rubin, 1983 ). The PS is formally defined as the conditional probability of receiving the treatment given the set of observed covariates X : PS = Pr( Z = 1 | X ).

Matching and PS designs usually investigate ATE = E [ Y i (1)] − E [ Y i (0)] or ATT = E [ Y i (1) | Z i = 1] – E [ Y i (0) | Z i = 1]. Both causal effects are identified if (a) the potential outcomes are statistically independent of the treatment indicator given the set of observed confounders X , { Y (1), Y (0)}⊥ Z | X ( unconfoundedness ; ⊥ denotes independence), and (b) the treatment probability is strictly between zero and one, 0 < Pr( Z = 1 | X ) < 1 ( positivity ).

By the positivity assumption we get E [ Y i (1)] = E X [ E [ Y i (1) | X ]] and E [ Y i (0)] = E X [ E [ Y i (0) | X ]]. If the unconfoundedness assumption holds, we can write the inner expectations as E [ Y i (1) | X ] = E [ Y i (1) | Z i =1; X ] and E [ Y i (0) | X ] = E [ Y i (0) | Z i = 0; X ]. Finally, because the treatment (control) outcomes of the treatment (control) subjects are actually observed, ATE is identified because it can be expressed in terms of observable quantities: ATE = E X [ E [ Y i | Z i = 1; X ]] – E X [ E [ Y i | Z i = 0; X ]]. The same can be shown for ATT. The unconfoundedness and positivity assumption are frequently referred to jointly as the strong ignorability assumption. Rosenbaum and Rubin (1983) proved that if the assignment is strongly ignorable given X , then it is also strongly ignorable given the PS alone.

Estimating ATE and ATT

Matching designs use a distance measure for matching each treatment subject to the closest control subject. The Mahalanobis distance is usually used for multivariate matching and the Euclidean distance on the logit of the PS for PS matching. Matching strategies differ with respect to the matching ratio (one-to-one or one-to-many), replacement of matched subjects (with or without replacement), use of a caliper (treatment subjects that do not have a control subject within a certain threshold remain unmatched), and the matching algorithm (greedy, genetic, or optimal matching; Sekhon, 2011 ; Steiner & Cook, 2013 ). Because we try to find at least one control subject for each treatment subject, matching estimators typically estimate ATT. Once treatment and control subjects are matched, ATT is computed as the difference in the mean outcome of the treatment and control group. An alternative matching strategy that allows for estimating ATE is full matching, which stratifies all subjects into the maximum number of strata, where each stratum contains at least one treatment and one control subject ( Hansen, 2004 ).

The PS can also be used for PS stratification and inverse-propensity weighting. PS stratification stratifies the treatment and control subjects into at least five strata and estimates the treatment effect within each stratum. ATE or ATT is then obtained as the weighted average of the stratum-specific treatment effects. Inverse-propensity weighting follows the same logic as inverse-probability weighting in survey research ( Horvitz & Thompson, 1952 ) and requires the computation of weights that refer to either the overall population (ATE) or the population of treated subjects only (ATT). Given the inverse-propensity weights, ATE or ATT is usually estimated via weighted least squares regression.

Because the true PSs are unknown, they need to be estimated from the observed data. The most common method for estimating the PS is logistic regression, which regresses the binary treatment indicator Z on predictors of the observed covariates. The PS model is specified according to balance criteria (instead of goodness of fit criteria), that is, the estimated PSs should remove all baseline differences in observed covariates ( Imbens & Rubin, 2015 ). The predicted probabilities from the PS model represent the estimated PSs.

All three PS designs—matching, stratification, and weighting—can benefit from additional covariance adjustments in an outcome regression. That is, for the matched, stratified or weighted data, the outcome is regressed on the treatment indicator and the additional covariates. Combining the PS design with a covariance adjustment gives researchers two chances to remove the confounding bias, by correctly specifying either the PS model or the outcome model. These combined methods are said to be doubly robust because they are robust against either the misspecification of the PS model or the misspecification of the outcome model ( Robins & Rotnitzky, 1995 ). The R packages optmatch ( Hansen & Klopfer, 2006 ) and MatchIt ( Ho et al., 2011 ) and the STATA command teffects , in particular teffects psmatch ( StataCorp, 2015 ), can be useful for matching or PS analyses.

The most challenging issue with matching and PS designs is the selection of covariates for establishing unconfoundedness. Ideally, subject-matter theory about the selection process and the outcome-generating model is used for selecting a set of covariates that removes all the confounding ( Pearl, 2009 ). If strong subject-matter theories are not available, selecting the right covariates is difficult. In the hope to remove a major part of the confounding bias—if not all of it—a frequently applied strategy is to match on as many covariates as possible. However, recent literature shows that thoughtless inclusion of covariates may increase rather than reduce the confounding bias ( Pearl, 2010 ; Steiner & Kim, in press). The risk of increasing bias can be reduced if the observed covariates cover a broad range of heterogeneous construct domains, including at least one reliable pretest measure of the outcome ( Steiner, Cook, et al., 2015 ). Besides having the right covariates, they also need to be reliably measured. The unreliable measurement of confounding covariates has a similar effect as the omission of a confounder: It results in a violation of the unconfoundedness assumption and thus in a biased effect estimate ( Steiner, Cook, & Shadish, 2011 ; Steiner & Kim, in press ).

Even if the set of reliably measured covariates establishes unconfoundedness, we still need to correctly specify the functional form of the PS model. Although parametric models like logistic regression, including higher order terms, might frequently approximate the correct functional form, they still rely on the linearity assumption. The linearity assumption can be relaxed if one estimates the PS with statistical learning algorithms like classification trees, neural networks, or the LASSO ( Keller, Kim, & Steiner, 2015 ; McCaffrey, Ridgeway, & Morral, 2004 ).

Strengthening Matching and PS Designs

The credibility of matching and PS designs heavily relies on the unconfoundedness assumption. Although empirically untestable, there are indirect ways for assessing unconfoundedness. First, unaffected (nonequivalent) outcomes that are known to be unaffected by the treatment can be used ( Shadish et al., 2002 ). For instance, we may expect that attendance in the science camp does not significantly affect the reading score. Thus, if we observe a significant group difference in the reading score after the PS adjustment, bias due to unobserved confounders (e.g., general intelligence) is still likely. Second, adding a second but conceptually different control group allows for a similar test as with the unaffected outcome ( Rosenbaum, 2002 ).

Because researchers rarely know whether the unconfoundedness assumption is actually met with the data at hand, it is important to assess the effect estimate’s sensitivity to potentially unobserved confounders. Sensitivity analyses investigate how strongly an estimate’s magnitude and significance changes if a confounder of a certain strength would have been omitted from the analyses. Causal conclusions are much more credible if the effect’s direction, magnitude, and significance is rather insensitive to omitted confounders ( Rosenbaum, 2002 ). However, despite the value of sensitivity analyses, they are not informative about whether hidden bias is actually present.

Schafer and Kang (2008) and Steiner and Cook (2013) provided a comprehensive introduction. Rigorous formalization and technical details of PS designs can be found in Imbens and Rubin (2015) . Rosenbaum (2002) discussed many important design issues in these designs.

COMPARATIVE INTERRUPTED TIME SERIES DESIGN

The designs discussed so far require researchers to have either full control over treatment assignment or reliable knowledge of the exogenous (IV) or endogenous part of the selection mechanism (i.e., the confounders). If none of these requirements are met, a comparative interrupted time series (CITS) design might be a viable alternative if (a) multiple measurements of the outcome ( time series ) are available for both the treatment and a comparison group and (b) the treatment group’s time series has been interrupted by an intervention.

Suppose that all students of one class in a school (say, an advanced science class) attend the camp, whereas all students of another class in the same school do not attend. Also assume that monthly measures of science achievement before and after the science camp are available. Figure 3 illustrates such a scenario where the x -axis represents time in Months and the y -axis the Science Score (aggregated at the class level). The filled symbols indicate the treatment group (science camp), open symbols the comparison group (no science camp). The science camp intervention divides both time series into a preintervention time series (circles) and a postintervention time series (squares). The changes in the levels and slopes of the pre- and postintervention regression lines represent the camp’s impact but possibly also the effect of other events that co-occur with the intervention. The dashed lines extrapolate the preintervention growth curves into the postintervention period, and thus represent the counterfactual situation where the intervention but also other co-occurring events are absent.

A hypothetical example of comparative interrupted time series design.

The strength of a CITS design is its ability to discriminate between the intervention’s effect and the effects of co-occurring events. Such events might be other potentially competing interventions (history effects) or changes in the measurement of the outcome (instrumentation), for instance. If the co-occurring events affect the treatment and comparison group to the same extent, then subtracting the changes in the comparison group’s growth curve from the changes in the treatment group’s growth curve provides a valid estimate of the intervention’s impact. Because we investigate the difference in the changes (= differences) of the two growth curves, the CITS design is a special case of the difference-in-differences design ( Somers et al., 2013 ).

Assume that a daily TV series about Albert Einstein was broadcast in the evenings of the science camp week and that students of both classes were exposed to the same extent to the TV series. It follows that the comparison group’s change in the growth curve represents the TV series’ impact. The comparison group’s time series in Figure 3 indicates that the TV series might have had an immediate impact on the growth curve’s level but almost no effect on the slope. On the other hand, the treatment group’s change in the growth curve is due to both the science camp and the TV series. Thus, in differencing out the TV series’ effect (estimated from the comparison group) we can identify the camp effect.

Let t c denote the time point of the intervention, then the intervention’s effect on the treated (ATT) at a postintervention time point t ≥ t c is defined as τ t = E [ Y i t T ( 1 ) ] − E [ Y i t T ( 0 ) ] , where Y i t T ( 0 ) and Y i t T ( 1 ) are the potential control and treatment outcomes of subject i in the treatment group ( T ) at time point t . The time series of the expected potential outcomes can be formalized as sum of nonparametric but additive time-dependent functions. The treatment group’s expected potential control outcome can be represented as E [ Y i t T ( 0 ) ] = f 0 T ( t ) + f E T ( t ) , where the control function f 0 T ( t ) generates the expected potential control outcomes in absence of any interventions ( I ) or co-occurring events ( E ), and the event function f E T ( t ) adds the effects of co-occurring events. Similarly, the expected potential treatment outcome can be written as E [ Y i t T ( 1 ) ] = f 0 T ( t ) + f E T ( t ) + f I T ( t ) , which adds the intervention’s effect τ t = f I T ( t ) to the control and event function. In the absence of a comparison group, we can try to identify the impact of the intervention by comparing the observable postintervention outcomes to the extrapolated outcomes from the preintervention time series (dashed line in Figure 3 ). Extrapolation is necessary because we do not observe any potential control outcomes in the postintervention period (only potential treatment outcomes are observed). Let f ^ 0 T ( t ) denote the parametric extrapolation of the preintervention control function f 0 T ( t ) , then the observable pre–post-intervention difference ( PP T ) in the expected control outcome is P P t T = f 0 T ( t ) + f E T ( t ) + f I T ( t ) − f ^ 0 T ( t ) = f I T ( t ) + ( f 0 T ( t ) − f ^ 0 T ( t ) ) + f E T ( t ) . Thus, in the absence of a comparison group, ATT is identified (i.e., P P t T = f I T ( t ) = τ t ) only if the control function is correctly specified ( f 0 T ( t ) = f ^ 0 T ( t ) ) and if no co-occurring events are present ( f E T ( t ) = 0 ).

The comparison group in a CITS design allows us to relax both of these identifying assumptions. In order to see this, we first define the expected control outcomes of the comparison group ( C ) as a sum of two time-dependent functions as before: E [ Y i t C ( 0 ) ] = f 0 C ( t ) + f E C ( t ) . Then, in extrapolating the comparison group’s preintervention function into the postintervention period, f ^ 0 C ( t ) , we can compute the pre–post-intervention difference for the comparison group: P P t C = f 0 C ( t ) + f E C ( t ) − f ^ 0 C ( t ) = f E C ( t ) + ( f 0 C ( t ) − f ^ 0 C ( t ) ) If the control function is correctly specified f 0 C ( t ) = f ^ 0 C ( t ) , the effect of co-occurring events is identified P P t C = f E C ( t ) . However, we do not necessarily need a correctly specified control function, because in a CITS design we focus on the difference in the treatment and comparison group’s pre–post-intervention differences, that is, P P t T − P P t C = f I T ( t ) + { ( f 0 T ( t ) − f ^ 0 T ( t ) ) − ( f 0 C ( t ) − f ^ 0 C ( t ) ) } + { f E T ( t ) − f E C ( t ) } . Thus, ATT is identified, P P t T − P P t C = f I T ( t ) = τ t , if (a) both control functions are either correctly specified or misspecified to the same additive extent such that ( f 0 T ( t ) − f ^ 0 T ( t ) ) = ( f 0 C ( t ) − f ^ 0 C ( t ) ) ( no differential misspecification ) and (b) the effect of co-occurring events is identical in the treatment and comparison group, f E T ( t ) = f E C ( t ) ( no differential event effects ).

Estimating ATT

CITS designs are typically analyzed with linear regression models that regress the outcome Y on the centered time variable ( T – t c ), the intervention indicator Z ( Z = 0 if t < t c , otherwise Z = 1), the group indicator G ( G = 1 for the treatment group and G = 0 for the control group), and the corresponding two-way and three-way interactions:

Depending on the number of subjects in each group, fixed or random effects for the subjects are included as well (time fixed or random effect can also be considered). β ^ 5 estimates the intervention’s immediate effect at the onset of the intervention (change in intercept) and β ^ 7 the intervention’s effect on the growth rate (change in slope). The inclusion of dummy variables for each postintervention time point (plus their interaction with the intervention and group indicators) would allow for a direct estimation of the time-specific effects. If the time series are long enough (at least 100 time points), then a more careful modeling of the autocorrelation structure via time series models should be considered.

Compared to other designs, CITS designs heavily rely on extrapolation and thus on functional form assumptions. Therefore, it is crucial that the functional forms of the pre- and postintervention time series (including their extrapolations) are correctly specified or at least not differentially misspecified. With short time series or measurement points that inadequately capture periodical variations, the correct specification of the functional form is very challenging. Another specification aspect concerns serial dependencies among the data points. Failing to model serial dependencies can bias effect estimates and their standard errors such that significance tests might be misleading. Accounting for serial dependencies requires autoregressive models (e.g., ARIMA models), but the time series should have at least 100 time points ( West, Biesanz, & Pitts, 2000 ). Standard fixed effects or random effects models deal at least partially with the dependence structure. Robust standard errors (e.g., Huber-White corrected ones) or the bootstrap can also be used to account for dependency structures.

Events that co-occur with the intervention of interest, like history or instrumentation effects, are a major threat to the time series designs that lack a comparison group ( Shadish et al., 2002 ). CITS designs are rather robust to co-occurring events as long as the treatment and comparison groups are affected to the same additive extent. However, there is no guarantee that both groups are exposed to the same events and affected to the same extent. For example, if students who do not attend the camp are less likely to watch the TV series, its effect cannot be completely differenced out (unless the exposure to the TV series is measured). If one uses aggregated data like class or school averages of achievement scores, then differential compositional shifts over time can also invalidate the CITS design. Compositional shifts occur due to dropouts or incoming subjects over time.

Strengthening CITS Designs

If the treatment and comparison group’s preintervention time series are very different (different levels and slopes), then the assumption that history or instrumentation threats affect both groups to the same additive extent may not hold. Matching treatment and comparison subjects prior to the analysis can increase the plausibility of this assumption. Instead of using all nonparticipating students of the comparison class, we may select only those students who have a similar level and growth in the preintervention science scores as the students participating in the camp. We can also match on additional covariates like socioeconomic status or motivation levels. Multivariate or PS matching can be used for this purpose. If the two groups are similar, it is more likely that they are affected by co-occurring events to the same extent.

As with the matching and PS designs, using an unaffected outcome in CITS designs helps to probe the untestable assumptions ( Coryn & Hobson, 2011 ; Shadish et al., 2002 ). For instance, we might expect that attending the science camp does not affect students’ reading scores but that some validity threats (e.g., attrition) operate on both the reading and science outcome. If we find a significant camp effect on the reading score, the validity of the CITS design for evaluating the camp’s impact on the science score is in doubt.

Another strategy to avoid validity threats is to control the time point of the intervention if possible. Researchers can wait with the implementation of the treatment until they have enough preintervention measures for reliably estimating the functional form. They can also choose to intervene when threats to validity are less likely (avoiding the week of the TV series). Control over the intervention also allows researchers to introduce and remove the treatment in subsequent time intervals, maybe even with switching replications between two (or more) groups. If the treatment is effective, we expect that the pattern of the intervention scheme is directly reflected in the time series of the outcome (for more details, see Shadish et al., 2002 ; for the literature on single case designs, see Kazdin, 2011 ).

A comprehensive introduction to CITS design can be found in Shadish et al. (2002) , which also addresses many classical applications. For more technical details of its identification, refer to Lechner (2011) . Wong, Cook, and Steiner (2009) evaluated the effect of No Child Left Behind using a CITS design.

CONCLUDING REMARKS

This article discussed four of the strongest quasi-experimental designs for causal inference when randomized experiments are not feasible. For each design we highlighted the identification strategies and the required assumptions. In practice, it is crucial that the design assumptions are met, otherwise biased effect estimates result. Because most important assumptions like the exclusion restriction or the unconfoundedness assumption are not directly testable, researchers should always try to assess their plausibility via indirect tests and investigate the effect estimates’ sensitivity to violations of these assumptions.

Our discussion of RD, IV, PS, and CITS designs made it also very clear that, in comparison to RCTs, quasi-experimental designs rely on more or stronger assumptions. With prefect control over treatment assignment and treatment implementation (as in an RCT), causal inference is warranted by a minimal set of assumptions. But with limited control over and knowledge about treatment assignment and implementation, stronger assumptions are required and causal effects might be identifiable only for local subpopulations. Nonetheless, observational data sometimes meet the assumptions of a quasi-experimental design, at least approximately, such that causal conclusions are credible. If so, the estimates of quasi-experimental designs—which exploit naturally occurring selection processes and real-world implementations of the treatment—are frequently better generalizable than the results from a controlled laboratory experiment. Thus, if external validity is a major concern, the results of randomized experiments should always be complemented by findings from valid quasi-experiments.

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• Health and social care
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Quasi-experimental study: comparative studies

How to use a quasi-experimental study to evaluate your digital health product.

Experimental and quasi-experimental studies can both be used to evaluate whether a digital health product achieves its aims. Randomised controlled trials are classed as experiments. They provide a high level of evidence for the relationship between cause (your digital product) and effect (the outcomes). There are particular things you must do to demonstrate cause and effect, such as randomising participants to groups. A quasi-experiment lacks at least one of these requirements; for example, you are unable to assign your participants to groups. However, quasi-experimental studies can still be used to evaluate how well your product is working.

The phrase ‘quasi-experimental’ often refers to the approach taken rather than a specific method. There are several designs of quasi-experimental studies.

What to use it for

A quasi-experimental study can help you to find out whether your digital product or service achieves its aims, so it can be useful when you have developed your product (summative evaluation). Quasi-experimental methods are often used in economic studies. You could also use them during development (formative or iterative evaluation) to find out how you can improve your product.

Benefits of quasi-experiments include:

• they can mimic an experiment and provide a high level of evidence without randomisation
• there are several designs to choose from that you can adapt depending on your context
• they can be used when there are practical or ethical reasons why participants can’t be randomised

Drawbacks of quasi-experiments include:

• you cannot rule out that other factors out of your control caused the results of your evaluation, although you can minimise this risk
• choosing an appropriate comparison group can be difficult

How to carry out a quasi-experimental study

There are 3 requirements for demonstrating cause and effect:

• randomisation – participants are randomly allocated to groups to make sure the groups are as similar to each other as possible, allowing comparison
• control – a control group is used to compare with the group receiving the product or intervention
• manipulation – the researcher manipulates aspects of what happens, such as assigning participants to different groups

These features make sure that your product has caused the outcomes you found. Otherwise, you cannot rule out that other influencing factors may have distorted your results and conclusions:

Confounding variables

Confounding variables are other variables that might influence the results. If participants in different groups systematically differ on these variables, the difference in outcomes between the groups may be because of the confounding variable rather than the experimental manipulation. The only way to get rid of all confounding variables is through randomisation because when we randomise, the variables will be present in equal numbers in both groups, even if we haven’t identified what these confounding variables are.

Bias means any process that produces systematic errors in the study, for example, errors in recruiting participants, collecting data or analysis, and drawing conclusions. This influences the results and conclusions of your study.

When you carry out a quasi-experimental study you should minimise biases and confounders. If you cannot randomise, you can increase the strength of your research design by:

• comparing your participants to an appropriate group that did not have access to your digital product
• measuring your outcomes before and after your product was introduced

Based on these 3 routes, here is an overview of different types of quasi-experimental designs.

Quasi-experimental designs with a comparison

One way to increase the strength of your results is by finding a comparison group that has similar attributes to your participants and then comparing the outcomes between the groups.

Because you have not randomly assigned participants, pre-existing differences between the people who had access to your product and those who did not may exist. These are called selection differences. It is important to choose your comparison appropriately to reduce this.

For example, if your digital product was introduced in one region, you could compare outcomes in another region. However, people in different regions may have different outcomes for other reasons (confounding variables). One region may be wealthier than another or have better access to alternative health services. The age profile may be different. You could consider what confounding variables might exist and pick a comparison region that has a similar profile.

Quasi-experimental designs with a before-after assessment

In this design, you assess outcomes for participants both before and after your product is introduced, and then compare. This is another way to minimise the effects of not randomly assigning participants.

Potential differences between participants in your evaluation could still have an impact on the results, but assessing participants before they used your product helps to decrease the influence of confounders and biases.

Be aware of additional issues associated with observing participants over time, for example:

• testing effects – participants’ scores are influenced by them repeating the same tests
• regression towards the mean – if you select participants on the basis that they have high or low scores on some measure, their scores may become more moderate over time because their initial extreme score was just random chance
• background changes – for example, demand for a service may be increasing over time, putting stresses on the service and leading to poorer outcomes

Time series designs

These quasi-experiments involve repeating data collection at many points in time before and after treatment.

There are a variety of designs that use time series:

• basic time series – assesses outcomes multiple times before and after your digital product is introduced
• control time series – introduces results from a comparison group
• turning the intervention on and off throughout the study to compare the effects
• interrupted time series – collects data before and after an interruption

In the analysis, the patterns of change over time are compared.

Digital technology is particularly suitable for time series design because digital devices allow you to collect data automatically and frequently. Ecological momentary assessment can be used to collect data.

By including multiple before-and-after assessments, you may be able to minimise problems of the weaker designs, such as simple one group before/after designs described above. There are also different ways to increase the strength of your design, for example by introducing multiple baselines.

Quasi-experimental designs with comparison and before-after assessment

Both including a comparison group and conducting a before-after assessment of the outcomes increases the strength of your design. This gives you greater confidence that your results are caused by the digital product you introduced.

Remember that not randomly assigning participants to the comparison groups and repeated measurements create some challenges with this design compared to a randomised experimental design.

If you cannot use comparison or before-after assessment

If there is no appropriate comparison group and you cannot compare participants before and after your digital product was introduced, drawing any conclusions around cause and effect of your digital product will be challenging.

This type of quasi-experimental design is most susceptible to biases and confounders that may affect the results of your evaluation. Still, using a design with one group and only testing participants after they receive the intervention will give you some insights about how your product is performing and will give you valuable directions for designing a stronger evaluation plan.

Causal methods

Causal inference methods use statistical methods to try and infer causal relationships from data that does not come from an experiment. They rely on identifying any confounding variables and on data being available for individuals for these variables. Read Pearl (2010), An introduction to causal inference for more information.

Examples of quasi-experimental methods

Case-control study , interrupted time-series , N-of-1 , before-and-after study and ecological momentary assessment can be seen as examples of quasi-experimental methods.

More information and resources

Sage research methods (2010), Quasi-experimental design . This explores the threats to the validity of quasi-experimental studies that you want to look out for when designing your study.

Pearl (2010), An introduction to causal inference . Information about causal methods.

Examples of quasi-experimental studies in digital health

Faudjar and others (2020), Field testing of a digital health information system for primary health care: A quasi-experimental study from India . Researchers developed a comprehensive digital tool for primary care and used a quasi-experimental study to evaluate it by comparing 2 communities.

Mitchel and others (2020), Commercial app use linked with sustained physical activity in two Canadian provinces: a 12-month quasi-experimental study . This study assessed one group before and after they gained access to an app that gives incentives for engaging in physical activity.

Peyman and others (2018), Digital Media-based Health Intervention on the promotion of Women’s physical activity: a quasi-experimental study . Researchers wanted to evaluate the impact of digital health on promoting physical activity in women. Eight active health centres were randomly selected to the intervention and control.

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Frequently asked questions

When should i use a quasi-experimental design.

Quasi-experimental design is most useful in situations where it would be unethical or impractical to run a true experiment .

Quasi-experiments have lower internal validity than true experiments, but they often have higher external validity  as they can use real-world interventions instead of artificial laboratory settings.

Frequently asked questions: Methodology

Attrition refers to participants leaving a study. It always happens to some extent—for example, in randomized controlled trials for medical research.

Differential attrition occurs when attrition or dropout rates differ systematically between the intervention and the control group . As a result, the characteristics of the participants who drop out differ from the characteristics of those who stay in the study. Because of this, study results may be biased .

Action research is conducted in order to solve a particular issue immediately, while case studies are often conducted over a longer period of time and focus more on observing and analyzing a particular ongoing phenomenon.

Action research is focused on solving a problem or informing individual and community-based knowledge in a way that impacts teaching, learning, and other related processes. It is less focused on contributing theoretical input, instead producing actionable input.

Action research is particularly popular with educators as a form of systematic inquiry because it prioritizes reflection and bridges the gap between theory and practice. Educators are able to simultaneously investigate an issue as they solve it, and the method is very iterative and flexible.

A cycle of inquiry is another name for action research . It is usually visualized in a spiral shape following a series of steps, such as “planning → acting → observing → reflecting.”

To make quantitative observations , you need to use instruments that are capable of measuring the quantity you want to observe. For example, you might use a ruler to measure the length of an object or a thermometer to measure its temperature.

Criterion validity and construct validity are both types of measurement validity . In other words, they both show you how accurately a method measures something.

While construct validity is the degree to which a test or other measurement method measures what it claims to measure, criterion validity is the degree to which a test can predictively (in the future) or concurrently (in the present) measure something.

Construct validity is often considered the overarching type of measurement validity . You need to have face validity , content validity , and criterion validity in order to achieve construct validity.

Convergent validity and discriminant validity are both subtypes of construct validity . Together, they help you evaluate whether a test measures the concept it was designed to measure.

• Convergent validity indicates whether a test that is designed to measure a particular construct correlates with other tests that assess the same or similar construct.
• Discriminant validity indicates whether two tests that should not be highly related to each other are indeed not related. This type of validity is also called divergent validity .

You need to assess both in order to demonstrate construct validity. Neither one alone is sufficient for establishing construct validity.

• Discriminant validity indicates whether two tests that should not be highly related to each other are indeed not related

Content validity shows you how accurately a test or other measurement method taps  into the various aspects of the specific construct you are researching.

In other words, it helps you answer the question: “does the test measure all aspects of the construct I want to measure?” If it does, then the test has high content validity.

The higher the content validity, the more accurate the measurement of the construct.

If the test fails to include parts of the construct, or irrelevant parts are included, the validity of the instrument is threatened, which brings your results into question.

Face validity and content validity are similar in that they both evaluate how suitable the content of a test is. The difference is that face validity is subjective, and assesses content at surface level.

When a test has strong face validity, anyone would agree that the test’s questions appear to measure what they are intended to measure.

For example, looking at a 4th grade math test consisting of problems in which students have to add and multiply, most people would agree that it has strong face validity (i.e., it looks like a math test).

On the other hand, content validity evaluates how well a test represents all the aspects of a topic. Assessing content validity is more systematic and relies on expert evaluation. of each question, analyzing whether each one covers the aspects that the test was designed to cover.

A 4th grade math test would have high content validity if it covered all the skills taught in that grade. Experts(in this case, math teachers), would have to evaluate the content validity by comparing the test to the learning objectives.

Snowball sampling is a non-probability sampling method . Unlike probability sampling (which involves some form of random selection ), the initial individuals selected to be studied are the ones who recruit new participants.

Because not every member of the target population has an equal chance of being recruited into the sample, selection in snowball sampling is non-random.

Snowball sampling is a non-probability sampling method , where there is not an equal chance for every member of the population to be included in the sample .

This means that you cannot use inferential statistics and make generalizations —often the goal of quantitative research . As such, a snowball sample is not representative of the target population and is usually a better fit for qualitative research .

Snowball sampling relies on the use of referrals. Here, the researcher recruits one or more initial participants, who then recruit the next ones.

Participants share similar characteristics and/or know each other. Because of this, not every member of the population has an equal chance of being included in the sample, giving rise to sampling bias .

Snowball sampling is best used in the following cases:

• If there is no sampling frame available (e.g., people with a rare disease)
• If the population of interest is hard to access or locate (e.g., people experiencing homelessness)
• If the research focuses on a sensitive topic (e.g., extramarital affairs)

The reproducibility and replicability of a study can be ensured by writing a transparent, detailed method section and using clear, unambiguous language.

Reproducibility and replicability are related terms.

• Reproducing research entails reanalyzing the existing data in the same manner.
• Replicating (or repeating ) the research entails reconducting the entire analysis, including the collection of new data . 
• A successful reproduction shows that the data analyses were conducted in a fair and honest manner.
• A successful replication shows that the reliability of the results is high.

Stratified sampling and quota sampling both involve dividing the population into subgroups and selecting units from each subgroup. The purpose in both cases is to select a representative sample and/or to allow comparisons between subgroups.

The main difference is that in stratified sampling, you draw a random sample from each subgroup ( probability sampling ). In quota sampling you select a predetermined number or proportion of units, in a non-random manner ( non-probability sampling ).

Purposive and convenience sampling are both sampling methods that are typically used in qualitative data collection.

A convenience sample is drawn from a source that is conveniently accessible to the researcher. Convenience sampling does not distinguish characteristics among the participants. On the other hand, purposive sampling focuses on selecting participants possessing characteristics associated with the research study.

The findings of studies based on either convenience or purposive sampling can only be generalized to the (sub)population from which the sample is drawn, and not to the entire population.

Random sampling or probability sampling is based on random selection. This means that each unit has an equal chance (i.e., equal probability) of being included in the sample.

On the other hand, convenience sampling involves stopping people at random, which means that not everyone has an equal chance of being selected depending on the place, time, or day you are collecting your data.

Convenience sampling and quota sampling are both non-probability sampling methods. They both use non-random criteria like availability, geographical proximity, or expert knowledge to recruit study participants.

However, in convenience sampling, you continue to sample units or cases until you reach the required sample size.

In quota sampling, you first need to divide your population of interest into subgroups (strata) and estimate their proportions (quota) in the population. Then you can start your data collection, using convenience sampling to recruit participants, until the proportions in each subgroup coincide with the estimated proportions in the population.

A sampling frame is a list of every member in the entire population . It is important that the sampling frame is as complete as possible, so that your sample accurately reflects your population.

Stratified and cluster sampling may look similar, but bear in mind that groups created in cluster sampling are heterogeneous , so the individual characteristics in the cluster vary. In contrast, groups created in stratified sampling are homogeneous , as units share characteristics.

Relatedly, in cluster sampling you randomly select entire groups and include all units of each group in your sample. However, in stratified sampling, you select some units of all groups and include them in your sample. In this way, both methods can ensure that your sample is representative of the target population .

A systematic review is secondary research because it uses existing research. You don’t collect new data yourself.

The key difference between observational studies and experimental designs is that a well-done observational study does not influence the responses of participants, while experiments do have some sort of treatment condition applied to at least some participants by random assignment .

An observational study is a great choice for you if your research question is based purely on observations. If there are ethical, logistical, or practical concerns that prevent you from conducting a traditional experiment , an observational study may be a good choice. In an observational study, there is no interference or manipulation of the research subjects, as well as no control or treatment groups .

It’s often best to ask a variety of people to review your measurements. You can ask experts, such as other researchers, or laypeople, such as potential participants, to judge the face validity of tests.

While experts have a deep understanding of research methods , the people you’re studying can provide you with valuable insights you may have missed otherwise.

Face validity is important because it’s a simple first step to measuring the overall validity of a test or technique. It’s a relatively intuitive, quick, and easy way to start checking whether a new measure seems useful at first glance.

Good face validity means that anyone who reviews your measure says that it seems to be measuring what it’s supposed to. With poor face validity, someone reviewing your measure may be left confused about what you’re measuring and why you’re using this method.

Face validity is about whether a test appears to measure what it’s supposed to measure. This type of validity is concerned with whether a measure seems relevant and appropriate for what it’s assessing only on the surface.

Statistical analyses are often applied to test validity with data from your measures. You test convergent validity and discriminant validity with correlations to see if results from your test are positively or negatively related to those of other established tests.

You can also use regression analyses to assess whether your measure is actually predictive of outcomes that you expect it to predict theoretically. A regression analysis that supports your expectations strengthens your claim of construct validity .

When designing or evaluating a measure, construct validity helps you ensure you’re actually measuring the construct you’re interested in. If you don’t have construct validity, you may inadvertently measure unrelated or distinct constructs and lose precision in your research.

Construct validity is often considered the overarching type of measurement validity ,  because it covers all of the other types. You need to have face validity , content validity , and criterion validity to achieve construct validity.

Construct validity is about how well a test measures the concept it was designed to evaluate. It’s one of four types of measurement validity , which includes construct validity, face validity , and criterion validity.

There are two subtypes of construct validity.

• Convergent validity : The extent to which your measure corresponds to measures of related constructs
• Discriminant validity : The extent to which your measure is unrelated or negatively related to measures of distinct constructs

Naturalistic observation is a valuable tool because of its flexibility, external validity , and suitability for topics that can’t be studied in a lab setting.

The downsides of naturalistic observation include its lack of scientific control , ethical considerations , and potential for bias from observers and subjects.

Naturalistic observation is a qualitative research method where you record the behaviors of your research subjects in real world settings. You avoid interfering or influencing anything in a naturalistic observation.

You can think of naturalistic observation as “people watching” with a purpose.

A dependent variable is what changes as a result of the independent variable manipulation in experiments . It’s what you’re interested in measuring, and it “depends” on your independent variable.

In statistics, dependent variables are also called:

• Response variables (they respond to a change in another variable)
• Outcome variables (they represent the outcome you want to measure)
• Left-hand-side variables (they appear on the left-hand side of a regression equation)

An independent variable is the variable you manipulate, control, or vary in an experimental study to explore its effects. It’s called “independent” because it’s not influenced by any other variables in the study.

Independent variables are also called:

• Explanatory variables (they explain an event or outcome)
• Predictor variables (they can be used to predict the value of a dependent variable)
• Right-hand-side variables (they appear on the right-hand side of a regression equation).

As a rule of thumb, questions related to thoughts, beliefs, and feelings work well in focus groups. Take your time formulating strong questions, paying special attention to phrasing. Be careful to avoid leading questions , which can bias your responses.

Overall, your focus group questions should be:

• Open-ended and flexible
• Impossible to answer with “yes” or “no” (questions that start with “why” or “how” are often best)
• Unambiguous, getting straight to the point while still stimulating discussion
• Unbiased and neutral

A structured interview is a data collection method that relies on asking questions in a set order to collect data on a topic. They are often quantitative in nature. Structured interviews are best used when: 

• You already have a very clear understanding of your topic. Perhaps significant research has already been conducted, or you have done some prior research yourself, but you already possess a baseline for designing strong structured questions.
• You are constrained in terms of time or resources and need to analyze your data quickly and efficiently.
• Your research question depends on strong parity between participants, with environmental conditions held constant.

More flexible interview options include semi-structured interviews , unstructured interviews , and focus groups .

Social desirability bias is the tendency for interview participants to give responses that will be viewed favorably by the interviewer or other participants. It occurs in all types of interviews and surveys , but is most common in semi-structured interviews , unstructured interviews , and focus groups .

Social desirability bias can be mitigated by ensuring participants feel at ease and comfortable sharing their views. Make sure to pay attention to your own body language and any physical or verbal cues, such as nodding or widening your eyes.

This type of bias can also occur in observations if the participants know they’re being observed. They might alter their behavior accordingly.

The interviewer effect is a type of bias that emerges when a characteristic of an interviewer (race, age, gender identity, etc.) influences the responses given by the interviewee.

There is a risk of an interviewer effect in all types of interviews , but it can be mitigated by writing really high-quality interview questions.

A semi-structured interview is a blend of structured and unstructured types of interviews. Semi-structured interviews are best used when:

• You have prior interview experience. Spontaneous questions are deceptively challenging, and it’s easy to accidentally ask a leading question or make a participant uncomfortable.
• Your research question is exploratory in nature. Participant answers can guide future research questions and help you develop a more robust knowledge base for future research.

An unstructured interview is the most flexible type of interview, but it is not always the best fit for your research topic.

Unstructured interviews are best used when:

• You are an experienced interviewer and have a very strong background in your research topic, since it is challenging to ask spontaneous, colloquial questions.
• Your research question is exploratory in nature. While you may have developed hypotheses, you are open to discovering new or shifting viewpoints through the interview process.
• You are seeking descriptive data, and are ready to ask questions that will deepen and contextualize your initial thoughts and hypotheses.
• Your research depends on forming connections with your participants and making them feel comfortable revealing deeper emotions, lived experiences, or thoughts.

The four most common types of interviews are:

• Structured interviews : The questions are predetermined in both topic and order. 
• Semi-structured interviews : A few questions are predetermined, but other questions aren’t planned.
• Unstructured interviews : None of the questions are predetermined.
• Focus group interviews : The questions are presented to a group instead of one individual.

Deductive reasoning is commonly used in scientific research, and it’s especially associated with quantitative research .

In research, you might have come across something called the hypothetico-deductive method . It’s the scientific method of testing hypotheses to check whether your predictions are substantiated by real-world data.

Deductive reasoning is a logical approach where you progress from general ideas to specific conclusions. It’s often contrasted with inductive reasoning , where you start with specific observations and form general conclusions.

Deductive reasoning is also called deductive logic.

There are many different types of inductive reasoning that people use formally or informally.

Here are a few common types:

• Inductive generalization : You use observations about a sample to come to a conclusion about the population it came from.
• Statistical generalization: You use specific numbers about samples to make statements about populations.
• Causal reasoning: You make cause-and-effect links between different things.
• Sign reasoning: You make a conclusion about a correlational relationship between different things.
• Analogical reasoning: You make a conclusion about something based on its similarities to something else.

Inductive reasoning is a bottom-up approach, while deductive reasoning is top-down.

Inductive reasoning takes you from the specific to the general, while in deductive reasoning, you make inferences by going from general premises to specific conclusions.

In inductive research , you start by making observations or gathering data. Then, you take a broad scan of your data and search for patterns. Finally, you make general conclusions that you might incorporate into theories.

Inductive reasoning is a method of drawing conclusions by going from the specific to the general. It’s usually contrasted with deductive reasoning, where you proceed from general information to specific conclusions.

Inductive reasoning is also called inductive logic or bottom-up reasoning.

A hypothesis states your predictions about what your research will find. It is a tentative answer to your research question that has not yet been tested. For some research projects, you might have to write several hypotheses that address different aspects of your research question.

A hypothesis is not just a guess — it should be based on existing theories and knowledge. It also has to be testable, which means you can support or refute it through scientific research methods (such as experiments, observations and statistical analysis of data).

Triangulation can help:

• Reduce research bias that comes from using a single method, theory, or investigator
• Enhance validity by approaching the same topic with different tools
• Establish credibility by giving you a complete picture of the research problem

But triangulation can also pose problems:

• It’s time-consuming and labor-intensive, often involving an interdisciplinary team.
• Your results may be inconsistent or even contradictory.

There are four main types of triangulation :

• Data triangulation : Using data from different times, spaces, and people
• Investigator triangulation : Involving multiple researchers in collecting or analyzing data
• Theory triangulation : Using varying theoretical perspectives in your research
• Methodological triangulation : Using different methodologies to approach the same topic

Many academic fields use peer review , largely to determine whether a manuscript is suitable for publication. Peer review enhances the credibility of the published manuscript.

However, peer review is also common in non-academic settings. The United Nations, the European Union, and many individual nations use peer review to evaluate grant applications. It is also widely used in medical and health-related fields as a teaching or quality-of-care measure. 

Peer assessment is often used in the classroom as a pedagogical tool. Both receiving feedback and providing it are thought to enhance the learning process, helping students think critically and collaboratively.

Peer review can stop obviously problematic, falsified, or otherwise untrustworthy research from being published. It also represents an excellent opportunity to get feedback from renowned experts in your field. It acts as a first defense, helping you ensure your argument is clear and that there are no gaps, vague terms, or unanswered questions for readers who weren’t involved in the research process.

Peer-reviewed articles are considered a highly credible source due to this stringent process they go through before publication.

In general, the peer review process follows the following steps: 

• First, the author submits the manuscript to the editor.
• Reject the manuscript and send it back to author, or 
• Send it onward to the selected peer reviewer(s) 
• Next, the peer review process occurs. The reviewer provides feedback, addressing any major or minor issues with the manuscript, and gives their advice regarding what edits should be made. 
• Lastly, the edited manuscript is sent back to the author. They input the edits, and resubmit it to the editor for publication.

Exploratory research is often used when the issue you’re studying is new or when the data collection process is challenging for some reason.

You can use exploratory research if you have a general idea or a specific question that you want to study but there is no preexisting knowledge or paradigm with which to study it.

Exploratory research is a methodology approach that explores research questions that have not previously been studied in depth. It is often used when the issue you’re studying is new, or the data collection process is challenging in some way.

Explanatory research is used to investigate how or why a phenomenon occurs. Therefore, this type of research is often one of the first stages in the research process , serving as a jumping-off point for future research.

Exploratory research aims to explore the main aspects of an under-researched problem, while explanatory research aims to explain the causes and consequences of a well-defined problem.

Explanatory research is a research method used to investigate how or why something occurs when only a small amount of information is available pertaining to that topic. It can help you increase your understanding of a given topic.

Clean data are valid, accurate, complete, consistent, unique, and uniform. Dirty data include inconsistencies and errors.

Dirty data can come from any part of the research process, including poor research design , inappropriate measurement materials, or flawed data entry.

Data cleaning takes place between data collection and data analyses. But you can use some methods even before collecting data.

For clean data, you should start by designing measures that collect valid data. Data validation at the time of data entry or collection helps you minimize the amount of data cleaning you’ll need to do.

After data collection, you can use data standardization and data transformation to clean your data. You’ll also deal with any missing values, outliers, and duplicate values.

Every dataset requires different techniques to clean dirty data , but you need to address these issues in a systematic way. You focus on finding and resolving data points that don’t agree or fit with the rest of your dataset.

These data might be missing values, outliers, duplicate values, incorrectly formatted, or irrelevant. You’ll start with screening and diagnosing your data. Then, you’ll often standardize and accept or remove data to make your dataset consistent and valid.

Data cleaning is necessary for valid and appropriate analyses. Dirty data contain inconsistencies or errors , but cleaning your data helps you minimize or resolve these.

Without data cleaning, you could end up with a Type I or II error in your conclusion. These types of erroneous conclusions can be practically significant with important consequences, because they lead to misplaced investments or missed opportunities.

Data cleaning involves spotting and resolving potential data inconsistencies or errors to improve your data quality. An error is any value (e.g., recorded weight) that doesn’t reflect the true value (e.g., actual weight) of something that’s being measured.

In this process, you review, analyze, detect, modify, or remove “dirty” data to make your dataset “clean.” Data cleaning is also called data cleansing or data scrubbing.

Research misconduct means making up or falsifying data, manipulating data analyses, or misrepresenting results in research reports. It’s a form of academic fraud.

These actions are committed intentionally and can have serious consequences; research misconduct is not a simple mistake or a point of disagreement but a serious ethical failure.

Anonymity means you don’t know who the participants are, while confidentiality means you know who they are but remove identifying information from your research report. Both are important ethical considerations .

You can only guarantee anonymity by not collecting any personally identifying information—for example, names, phone numbers, email addresses, IP addresses, physical characteristics, photos, or videos.

You can keep data confidential by using aggregate information in your research report, so that you only refer to groups of participants rather than individuals.

Research ethics matter for scientific integrity, human rights and dignity, and collaboration between science and society. These principles make sure that participation in studies is voluntary, informed, and safe.

Ethical considerations in research are a set of principles that guide your research designs and practices. These principles include voluntary participation, informed consent, anonymity, confidentiality, potential for harm, and results communication.

Scientists and researchers must always adhere to a certain code of conduct when collecting data from others .

These considerations protect the rights of research participants, enhance research validity , and maintain scientific integrity.

In multistage sampling , you can use probability or non-probability sampling methods .

For a probability sample, you have to conduct probability sampling at every stage.

You can mix it up by using simple random sampling , systematic sampling , or stratified sampling to select units at different stages, depending on what is applicable and relevant to your study.

Multistage sampling can simplify data collection when you have large, geographically spread samples, and you can obtain a probability sample without a complete sampling frame.

But multistage sampling may not lead to a representative sample, and larger samples are needed for multistage samples to achieve the statistical properties of simple random samples .

These are four of the most common mixed methods designs :

• Convergent parallel: Quantitative and qualitative data are collected at the same time and analyzed separately. After both analyses are complete, compare your results to draw overall conclusions. 
• Embedded: Quantitative and qualitative data are collected at the same time, but within a larger quantitative or qualitative design. One type of data is secondary to the other.
• Explanatory sequential: Quantitative data is collected and analyzed first, followed by qualitative data. You can use this design if you think your qualitative data will explain and contextualize your quantitative findings.
• Exploratory sequential: Qualitative data is collected and analyzed first, followed by quantitative data. You can use this design if you think the quantitative data will confirm or validate your qualitative findings.

Triangulation in research means using multiple datasets, methods, theories and/or investigators to address a research question. It’s a research strategy that can help you enhance the validity and credibility of your findings.

Triangulation is mainly used in qualitative research , but it’s also commonly applied in quantitative research . Mixed methods research always uses triangulation.

In multistage sampling , or multistage cluster sampling, you draw a sample from a population using smaller and smaller groups at each stage.

This method is often used to collect data from a large, geographically spread group of people in national surveys, for example. You take advantage of hierarchical groupings (e.g., from state to city to neighborhood) to create a sample that’s less expensive and time-consuming to collect data from.

No, the steepness or slope of the line isn’t related to the correlation coefficient value. The correlation coefficient only tells you how closely your data fit on a line, so two datasets with the same correlation coefficient can have very different slopes.

To find the slope of the line, you’ll need to perform a regression analysis .

Correlation coefficients always range between -1 and 1.

The sign of the coefficient tells you the direction of the relationship: a positive value means the variables change together in the same direction, while a negative value means they change together in opposite directions.

The absolute value of a number is equal to the number without its sign. The absolute value of a correlation coefficient tells you the magnitude of the correlation: the greater the absolute value, the stronger the correlation.

These are the assumptions your data must meet if you want to use Pearson’s r :

• Both variables are on an interval or ratio level of measurement
• Data from both variables follow normal distributions
• Your data have no outliers
• Your data is from a random or representative sample
• You expect a linear relationship between the two variables

Quantitative research designs can be divided into two main categories:

• Correlational and descriptive designs are used to investigate characteristics, averages, trends, and associations between variables.
• Experimental and quasi-experimental designs are used to test causal relationships .

Qualitative research designs tend to be more flexible. Common types of qualitative design include case study , ethnography , and grounded theory designs.

A well-planned research design helps ensure that your methods match your research aims, that you collect high-quality data, and that you use the right kind of analysis to answer your questions, utilizing credible sources . This allows you to draw valid , trustworthy conclusions.

The priorities of a research design can vary depending on the field, but you usually have to specify:

• Your research questions and/or hypotheses
• Your overall approach (e.g., qualitative or quantitative )
• The type of design you’re using (e.g., a survey , experiment , or case study )
• Your sampling methods or criteria for selecting subjects
• Your data collection methods (e.g., questionnaires , observations)
• Your data collection procedures (e.g., operationalization , timing and data management)
• Your data analysis methods (e.g., statistical tests  or thematic analysis )

A research design is a strategy for answering your   research question . It defines your overall approach and determines how you will collect and analyze data.

Questionnaires can be self-administered or researcher-administered.

Self-administered questionnaires can be delivered online or in paper-and-pen formats, in person or through mail. All questions are standardized so that all respondents receive the same questions with identical wording.

Researcher-administered questionnaires are interviews that take place by phone, in-person, or online between researchers and respondents. You can gain deeper insights by clarifying questions for respondents or asking follow-up questions.

You can organize the questions logically, with a clear progression from simple to complex, or randomly between respondents. A logical flow helps respondents process the questionnaire easier and quicker, but it may lead to bias. Randomization can minimize the bias from order effects.

Closed-ended, or restricted-choice, questions offer respondents a fixed set of choices to select from. These questions are easier to answer quickly.

Open-ended or long-form questions allow respondents to answer in their own words. Because there are no restrictions on their choices, respondents can answer in ways that researchers may not have otherwise considered.

A questionnaire is a data collection tool or instrument, while a survey is an overarching research method that involves collecting and analyzing data from people using questionnaires.

The third variable and directionality problems are two main reasons why correlation isn’t causation .

The third variable problem means that a confounding variable affects both variables to make them seem causally related when they are not.

The directionality problem is when two variables correlate and might actually have a causal relationship, but it’s impossible to conclude which variable causes changes in the other.

Correlation describes an association between variables : when one variable changes, so does the other. A correlation is a statistical indicator of the relationship between variables.

Causation means that changes in one variable brings about changes in the other (i.e., there is a cause-and-effect relationship between variables). The two variables are correlated with each other, and there’s also a causal link between them.

While causation and correlation can exist simultaneously, correlation does not imply causation. In other words, correlation is simply a relationship where A relates to B—but A doesn’t necessarily cause B to happen (or vice versa). Mistaking correlation for causation is a common error and can lead to false cause fallacy .

Controlled experiments establish causality, whereas correlational studies only show associations between variables.

• In an experimental design , you manipulate an independent variable and measure its effect on a dependent variable. Other variables are controlled so they can’t impact the results.
• In a correlational design , you measure variables without manipulating any of them. You can test whether your variables change together, but you can’t be sure that one variable caused a change in another.

In general, correlational research is high in external validity while experimental research is high in internal validity .

A correlation is usually tested for two variables at a time, but you can test correlations between three or more variables.

A correlation coefficient is a single number that describes the strength and direction of the relationship between your variables.

Different types of correlation coefficients might be appropriate for your data based on their levels of measurement and distributions . The Pearson product-moment correlation coefficient (Pearson’s r ) is commonly used to assess a linear relationship between two quantitative variables.

A correlational research design investigates relationships between two variables (or more) without the researcher controlling or manipulating any of them. It’s a non-experimental type of quantitative research .

A correlation reflects the strength and/or direction of the association between two or more variables.

• A positive correlation means that both variables change in the same direction.
• A negative correlation means that the variables change in opposite directions.
• A zero correlation means there’s no relationship between the variables.

Random error  is almost always present in scientific studies, even in highly controlled settings. While you can’t eradicate it completely, you can reduce random error by taking repeated measurements, using a large sample, and controlling extraneous variables .

You can avoid systematic error through careful design of your sampling , data collection , and analysis procedures. For example, use triangulation to measure your variables using multiple methods; regularly calibrate instruments or procedures; use random sampling and random assignment ; and apply masking (blinding) where possible.

Systematic error is generally a bigger problem in research.

With random error, multiple measurements will tend to cluster around the true value. When you’re collecting data from a large sample , the errors in different directions will cancel each other out.

Systematic errors are much more problematic because they can skew your data away from the true value. This can lead you to false conclusions ( Type I and II errors ) about the relationship between the variables you’re studying.

Random and systematic error are two types of measurement error.

Random error is a chance difference between the observed and true values of something (e.g., a researcher misreading a weighing scale records an incorrect measurement).

Systematic error is a consistent or proportional difference between the observed and true values of something (e.g., a miscalibrated scale consistently records weights as higher than they actually are).

On graphs, the explanatory variable is conventionally placed on the x-axis, while the response variable is placed on the y-axis.

• If you have quantitative variables , use a scatterplot or a line graph.
• If your response variable is categorical, use a scatterplot or a line graph.
• If your explanatory variable is categorical, use a bar graph.

The term “ explanatory variable ” is sometimes preferred over “ independent variable ” because, in real world contexts, independent variables are often influenced by other variables. This means they aren’t totally independent.

Multiple independent variables may also be correlated with each other, so “explanatory variables” is a more appropriate term.

The difference between explanatory and response variables is simple:

• An explanatory variable is the expected cause, and it explains the results.
• A response variable is the expected effect, and it responds to other variables.

In a controlled experiment , all extraneous variables are held constant so that they can’t influence the results. Controlled experiments require:

• A control group that receives a standard treatment, a fake treatment, or no treatment.
• Random assignment of participants to ensure the groups are equivalent.

Depending on your study topic, there are various other methods of controlling variables .

There are 4 main types of extraneous variables :

• Demand characteristics : environmental cues that encourage participants to conform to researchers’ expectations.
• Experimenter effects : unintentional actions by researchers that influence study outcomes.
• Situational variables : environmental variables that alter participants’ behaviors.
• Participant variables : any characteristic or aspect of a participant’s background that could affect study results.

An extraneous variable is any variable that you’re not investigating that can potentially affect the dependent variable of your research study.

A confounding variable is a type of extraneous variable that not only affects the dependent variable, but is also related to the independent variable.

In a factorial design, multiple independent variables are tested.

If you test two variables, each level of one independent variable is combined with each level of the other independent variable to create different conditions.

Within-subjects designs have many potential threats to internal validity , but they are also very statistically powerful .

Advantages:

• Only requires small samples
• Statistically powerful
• Removes the effects of individual differences on the outcomes

Disadvantages:

• Internal validity threats reduce the likelihood of establishing a direct relationship between variables
• Time-related effects, such as growth, can influence the outcomes
• Carryover effects mean that the specific order of different treatments affect the outcomes

While a between-subjects design has fewer threats to internal validity , it also requires more participants for high statistical power than a within-subjects design .

• Prevents carryover effects of learning and fatigue.
• Shorter study duration.
• Needs larger samples for high power.
• Uses more resources to recruit participants, administer sessions, cover costs, etc.
• Individual differences may be an alternative explanation for results.

Yes. Between-subjects and within-subjects designs can be combined in a single study when you have two or more independent variables (a factorial design). In a mixed factorial design, one variable is altered between subjects and another is altered within subjects.

In a between-subjects design , every participant experiences only one condition, and researchers assess group differences between participants in various conditions.

In a within-subjects design , each participant experiences all conditions, and researchers test the same participants repeatedly for differences between conditions.

The word “between” means that you’re comparing different conditions between groups, while the word “within” means you’re comparing different conditions within the same group.

Random assignment is used in experiments with a between-groups or independent measures design. In this research design, there’s usually a control group and one or more experimental groups. Random assignment helps ensure that the groups are comparable.

In general, you should always use random assignment in this type of experimental design when it is ethically possible and makes sense for your study topic.

To implement random assignment , assign a unique number to every member of your study’s sample .

Then, you can use a random number generator or a lottery method to randomly assign each number to a control or experimental group. You can also do so manually, by flipping a coin or rolling a dice to randomly assign participants to groups.

Random selection, or random sampling , is a way of selecting members of a population for your study’s sample.

In contrast, random assignment is a way of sorting the sample into control and experimental groups.

Random sampling enhances the external validity or generalizability of your results, while random assignment improves the internal validity of your study.

In experimental research, random assignment is a way of placing participants from your sample into different groups using randomization. With this method, every member of the sample has a known or equal chance of being placed in a control group or an experimental group.

“Controlling for a variable” means measuring extraneous variables and accounting for them statistically to remove their effects on other variables.

Researchers often model control variable data along with independent and dependent variable data in regression analyses and ANCOVAs . That way, you can isolate the control variable’s effects from the relationship between the variables of interest.

Control variables help you establish a correlational or causal relationship between variables by enhancing internal validity .

If you don’t control relevant extraneous variables , they may influence the outcomes of your study, and you may not be able to demonstrate that your results are really an effect of your independent variable .

A control variable is any variable that’s held constant in a research study. It’s not a variable of interest in the study, but it’s controlled because it could influence the outcomes.

Including mediators and moderators in your research helps you go beyond studying a simple relationship between two variables for a fuller picture of the real world. They are important to consider when studying complex correlational or causal relationships.

Mediators are part of the causal pathway of an effect, and they tell you how or why an effect takes place. Moderators usually help you judge the external validity of your study by identifying the limitations of when the relationship between variables holds.

If something is a mediating variable :

• It’s caused by the independent variable .
• It influences the dependent variable
• When it’s taken into account, the statistical correlation between the independent and dependent variables is higher than when it isn’t considered.

A confounder is a third variable that affects variables of interest and makes them seem related when they are not. In contrast, a mediator is the mechanism of a relationship between two variables: it explains the process by which they are related.

A mediator variable explains the process through which two variables are related, while a moderator variable affects the strength and direction of that relationship.

There are three key steps in systematic sampling :

• Define and list your population , ensuring that it is not ordered in a cyclical or periodic order.
• Decide on your sample size and calculate your interval, k , by dividing your population by your target sample size.
• Choose every k th member of the population as your sample.

Systematic sampling is a probability sampling method where researchers select members of the population at a regular interval – for example, by selecting every 15th person on a list of the population. If the population is in a random order, this can imitate the benefits of simple random sampling .

Yes, you can create a stratified sample using multiple characteristics, but you must ensure that every participant in your study belongs to one and only one subgroup. In this case, you multiply the numbers of subgroups for each characteristic to get the total number of groups.

For example, if you were stratifying by location with three subgroups (urban, rural, or suburban) and marital status with five subgroups (single, divorced, widowed, married, or partnered), you would have 3 x 5 = 15 subgroups.

You should use stratified sampling when your sample can be divided into mutually exclusive and exhaustive subgroups that you believe will take on different mean values for the variable that you’re studying.

Using stratified sampling will allow you to obtain more precise (with lower variance ) statistical estimates of whatever you are trying to measure.

For example, say you want to investigate how income differs based on educational attainment, but you know that this relationship can vary based on race. Using stratified sampling, you can ensure you obtain a large enough sample from each racial group, allowing you to draw more precise conclusions.

In stratified sampling , researchers divide subjects into subgroups called strata based on characteristics that they share (e.g., race, gender, educational attainment).

Once divided, each subgroup is randomly sampled using another probability sampling method.

Cluster sampling is more time- and cost-efficient than other probability sampling methods , particularly when it comes to large samples spread across a wide geographical area.

However, it provides less statistical certainty than other methods, such as simple random sampling , because it is difficult to ensure that your clusters properly represent the population as a whole.

There are three types of cluster sampling : single-stage, double-stage and multi-stage clustering. In all three types, you first divide the population into clusters, then randomly select clusters for use in your sample.

• In single-stage sampling , you collect data from every unit within the selected clusters.
• In double-stage sampling , you select a random sample of units from within the clusters.
• In multi-stage sampling , you repeat the procedure of randomly sampling elements from within the clusters until you have reached a manageable sample.

Cluster sampling is a probability sampling method in which you divide a population into clusters, such as districts or schools, and then randomly select some of these clusters as your sample.

The clusters should ideally each be mini-representations of the population as a whole.

If properly implemented, simple random sampling is usually the best sampling method for ensuring both internal and external validity . However, it can sometimes be impractical and expensive to implement, depending on the size of the population to be studied,

If you have a list of every member of the population and the ability to reach whichever members are selected, you can use simple random sampling.

The American Community Survey  is an example of simple random sampling . In order to collect detailed data on the population of the US, the Census Bureau officials randomly select 3.5 million households per year and use a variety of methods to convince them to fill out the survey.

Simple random sampling is a type of probability sampling in which the researcher randomly selects a subset of participants from a population . Each member of the population has an equal chance of being selected. Data is then collected from as large a percentage as possible of this random subset.

A quasi-experiment is a type of research design that attempts to establish a cause-and-effect relationship. The main difference with a true experiment is that the groups are not randomly assigned.

Blinding is important to reduce research bias (e.g., observer bias , demand characteristics ) and ensure a study’s internal validity .

If participants know whether they are in a control or treatment group , they may adjust their behavior in ways that affect the outcome that researchers are trying to measure. If the people administering the treatment are aware of group assignment, they may treat participants differently and thus directly or indirectly influence the final results.

• In a single-blind study , only the participants are blinded.
• In a double-blind study , both participants and experimenters are blinded.
• In a triple-blind study , the assignment is hidden not only from participants and experimenters, but also from the researchers analyzing the data.

Blinding means hiding who is assigned to the treatment group and who is assigned to the control group in an experiment .

A true experiment (a.k.a. a controlled experiment) always includes at least one control group that doesn’t receive the experimental treatment.

However, some experiments use a within-subjects design to test treatments without a control group. In these designs, you usually compare one group’s outcomes before and after a treatment (instead of comparing outcomes between different groups).

For strong internal validity , it’s usually best to include a control group if possible. Without a control group, it’s harder to be certain that the outcome was caused by the experimental treatment and not by other variables.

An experimental group, also known as a treatment group, receives the treatment whose effect researchers wish to study, whereas a control group does not. They should be identical in all other ways.

Individual Likert-type questions are generally considered ordinal data , because the items have clear rank order, but don’t have an even distribution.

Overall Likert scale scores are sometimes treated as interval data. These scores are considered to have directionality and even spacing between them.

The type of data determines what statistical tests you should use to analyze your data.

A Likert scale is a rating scale that quantitatively assesses opinions, attitudes, or behaviors. It is made up of 4 or more questions that measure a single attitude or trait when response scores are combined.

To use a Likert scale in a survey , you present participants with Likert-type questions or statements, and a continuum of items, usually with 5 or 7 possible responses, to capture their degree of agreement.

In scientific research, concepts are the abstract ideas or phenomena that are being studied (e.g., educational achievement). Variables are properties or characteristics of the concept (e.g., performance at school), while indicators are ways of measuring or quantifying variables (e.g., yearly grade reports).

The process of turning abstract concepts into measurable variables and indicators is called operationalization .

There are various approaches to qualitative data analysis , but they all share five steps in common:

• Prepare and organize your data.
• Review and explore your data.
• Develop a data coding system.
• Assign codes to the data.
• Identify recurring themes.

The specifics of each step depend on the focus of the analysis. Some common approaches include textual analysis , thematic analysis , and discourse analysis .

There are five common approaches to qualitative research :

• Grounded theory involves collecting data in order to develop new theories.
• Ethnography involves immersing yourself in a group or organization to understand its culture.
• Narrative research involves interpreting stories to understand how people make sense of their experiences and perceptions.
• Phenomenological research involves investigating phenomena through people’s lived experiences.
• Action research links theory and practice in several cycles to drive innovative changes.

Hypothesis testing is a formal procedure for investigating our ideas about the world using statistics. It is used by scientists to test specific predictions, called hypotheses , by calculating how likely it is that a pattern or relationship between variables could have arisen by chance.

Operationalization means turning abstract conceptual ideas into measurable observations.

For example, the concept of social anxiety isn’t directly observable, but it can be operationally defined in terms of self-rating scores, behavioral avoidance of crowded places, or physical anxiety symptoms in social situations.

Before collecting data , it’s important to consider how you will operationalize the variables that you want to measure.

When conducting research, collecting original data has significant advantages:

• You can tailor data collection to your specific research aims (e.g. understanding the needs of your consumers or user testing your website)
• You can control and standardize the process for high reliability and validity (e.g. choosing appropriate measurements and sampling methods )

However, there are also some drawbacks: data collection can be time-consuming, labor-intensive and expensive. In some cases, it’s more efficient to use secondary data that has already been collected by someone else, but the data might be less reliable.

Data collection is the systematic process by which observations or measurements are gathered in research. It is used in many different contexts by academics, governments, businesses, and other organizations.

There are several methods you can use to decrease the impact of confounding variables on your research: restriction, matching, statistical control and randomization.

In restriction , you restrict your sample by only including certain subjects that have the same values of potential confounding variables.

In matching , you match each of the subjects in your treatment group with a counterpart in the comparison group. The matched subjects have the same values on any potential confounding variables, and only differ in the independent variable .

In statistical control , you include potential confounders as variables in your regression .

In randomization , you randomly assign the treatment (or independent variable) in your study to a sufficiently large number of subjects, which allows you to control for all potential confounding variables.

A confounding variable is closely related to both the independent and dependent variables in a study. An independent variable represents the supposed cause , while the dependent variable is the supposed effect . A confounding variable is a third variable that influences both the independent and dependent variables.

Failing to account for confounding variables can cause you to wrongly estimate the relationship between your independent and dependent variables.

To ensure the internal validity of your research, you must consider the impact of confounding variables. If you fail to account for them, you might over- or underestimate the causal relationship between your independent and dependent variables , or even find a causal relationship where none exists.

Yes, but including more than one of either type requires multiple research questions .

For example, if you are interested in the effect of a diet on health, you can use multiple measures of health: blood sugar, blood pressure, weight, pulse, and many more. Each of these is its own dependent variable with its own research question.

You could also choose to look at the effect of exercise levels as well as diet, or even the additional effect of the two combined. Each of these is a separate independent variable .

To ensure the internal validity of an experiment , you should only change one independent variable at a time.

No. The value of a dependent variable depends on an independent variable, so a variable cannot be both independent and dependent at the same time. It must be either the cause or the effect, not both!

You want to find out how blood sugar levels are affected by drinking diet soda and regular soda, so you conduct an experiment .

• The type of soda – diet or regular – is the independent variable .
• The level of blood sugar that you measure is the dependent variable – it changes depending on the type of soda.

Determining cause and effect is one of the most important parts of scientific research. It’s essential to know which is the cause – the independent variable – and which is the effect – the dependent variable.

In non-probability sampling , the sample is selected based on non-random criteria, and not every member of the population has a chance of being included.

Common non-probability sampling methods include convenience sampling , voluntary response sampling, purposive sampling , snowball sampling, and quota sampling .

Probability sampling means that every member of the target population has a known chance of being included in the sample.

Probability sampling methods include simple random sampling , systematic sampling , stratified sampling , and cluster sampling .

Using careful research design and sampling procedures can help you avoid sampling bias . Oversampling can be used to correct undercoverage bias .

Some common types of sampling bias include self-selection bias , nonresponse bias , undercoverage bias , survivorship bias , pre-screening or advertising bias, and healthy user bias.

Sampling bias is a threat to external validity – it limits the generalizability of your findings to a broader group of people.

A sampling error is the difference between a population parameter and a sample statistic .

A statistic refers to measures about the sample , while a parameter refers to measures about the population .

Populations are used when a research question requires data from every member of the population. This is usually only feasible when the population is small and easily accessible.

Samples are used to make inferences about populations . Samples are easier to collect data from because they are practical, cost-effective, convenient, and manageable.

There are seven threats to external validity : selection bias , history, experimenter effect, Hawthorne effect , testing effect, aptitude-treatment and situation effect.

The two types of external validity are population validity (whether you can generalize to other groups of people) and ecological validity (whether you can generalize to other situations and settings).

The external validity of a study is the extent to which you can generalize your findings to different groups of people, situations, and measures.

Cross-sectional studies cannot establish a cause-and-effect relationship or analyze behavior over a period of time. To investigate cause and effect, you need to do a longitudinal study or an experimental study .

Cross-sectional studies are less expensive and time-consuming than many other types of study. They can provide useful insights into a population’s characteristics and identify correlations for further research.

Sometimes only cross-sectional data is available for analysis; other times your research question may only require a cross-sectional study to answer it.

Longitudinal studies can last anywhere from weeks to decades, although they tend to be at least a year long.

The 1970 British Cohort Study , which has collected data on the lives of 17,000 Brits since their births in 1970, is one well-known example of a longitudinal study .

Longitudinal studies are better to establish the correct sequence of events, identify changes over time, and provide insight into cause-and-effect relationships, but they also tend to be more expensive and time-consuming than other types of studies.

Longitudinal studies and cross-sectional studies are two different types of research design . In a cross-sectional study you collect data from a population at a specific point in time; in a longitudinal study you repeatedly collect data from the same sample over an extended period of time.

There are eight threats to internal validity : history, maturation, instrumentation, testing, selection bias , regression to the mean, social interaction and attrition .

Internal validity is the extent to which you can be confident that a cause-and-effect relationship established in a study cannot be explained by other factors.

In mixed methods research , you use both qualitative and quantitative data collection and analysis methods to answer your research question .

The research methods you use depend on the type of data you need to answer your research question .

• If you want to measure something or test a hypothesis , use quantitative methods . If you want to explore ideas, thoughts and meanings, use qualitative methods .
• If you want to analyze a large amount of readily-available data, use secondary data. If you want data specific to your purposes with control over how it is generated, collect primary data.
• If you want to establish cause-and-effect relationships between variables , use experimental methods. If you want to understand the characteristics of a research subject, use descriptive methods.

A confounding variable , also called a confounder or confounding factor, is a third variable in a study examining a potential cause-and-effect relationship.

A confounding variable is related to both the supposed cause and the supposed effect of the study. It can be difficult to separate the true effect of the independent variable from the effect of the confounding variable.

In your research design , it’s important to identify potential confounding variables and plan how you will reduce their impact.

Discrete and continuous variables are two types of quantitative variables :

• Discrete variables represent counts (e.g. the number of objects in a collection).
• Continuous variables represent measurable amounts (e.g. water volume or weight).

Quantitative variables are any variables where the data represent amounts (e.g. height, weight, or age).

Categorical variables are any variables where the data represent groups. This includes rankings (e.g. finishing places in a race), classifications (e.g. brands of cereal), and binary outcomes (e.g. coin flips).

You need to know what type of variables you are working with to choose the right statistical test for your data and interpret your results .

You can think of independent and dependent variables in terms of cause and effect: an independent variable is the variable you think is the cause , while a dependent variable is the effect .

In an experiment, you manipulate the independent variable and measure the outcome in the dependent variable. For example, in an experiment about the effect of nutrients on crop growth:

• The  independent variable  is the amount of nutrients added to the crop field.
• The  dependent variable is the biomass of the crops at harvest time.

Defining your variables, and deciding how you will manipulate and measure them, is an important part of experimental design .

Experimental design means planning a set of procedures to investigate a relationship between variables . To design a controlled experiment, you need:

• A testable hypothesis
• At least one independent variable that can be precisely manipulated
• At least one dependent variable that can be precisely measured

When designing the experiment, you decide:

• How you will manipulate the variable(s)
• How you will control for any potential confounding variables
• How many subjects or samples will be included in the study
• How subjects will be assigned to treatment levels

Experimental design is essential to the internal and external validity of your experiment.

I nternal validity is the degree of confidence that the causal relationship you are testing is not influenced by other factors or variables .

External validity is the extent to which your results can be generalized to other contexts.

The validity of your experiment depends on your experimental design .

Reliability and validity are both about how well a method measures something:

• Reliability refers to the  consistency of a measure (whether the results can be reproduced under the same conditions).
• Validity   refers to the  accuracy of a measure (whether the results really do represent what they are supposed to measure).

If you are doing experimental research, you also have to consider the internal and external validity of your experiment.

A sample is a subset of individuals from a larger population . Sampling means selecting the group that you will actually collect data from in your research. For example, if you are researching the opinions of students in your university, you could survey a sample of 100 students.

In statistics, sampling allows you to test a hypothesis about the characteristics of a population.

Quantitative research deals with numbers and statistics, while qualitative research deals with words and meanings.

Quantitative methods allow you to systematically measure variables and test hypotheses . Qualitative methods allow you to explore concepts and experiences in more detail.

Methodology refers to the overarching strategy and rationale of your research project . It involves studying the methods used in your field and the theories or principles behind them, in order to develop an approach that matches your objectives.

Methods are the specific tools and procedures you use to collect and analyze data (for example, experiments, surveys , and statistical tests ).

In shorter scientific papers, where the aim is to report the findings of a specific study, you might simply describe what you did in a methods section .

In a longer or more complex research project, such as a thesis or dissertation , you will probably include a methodology section , where you explain your approach to answering the research questions and cite relevant sources to support your choice of methods.

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Why use a quasi experimental design when you can do an experiment?

I read about quasi-experimental design and the variations it has such as pre-test post-test non-equivalent groups , and also experimental designs . Having compared these two, I ascertained that the difference between this variation of quasi-experimental design( pre-test post-test non-equivalent groups ) and experimental design is randomization. However, what I couldn't understand was:

Why should quasi-experimental design even exist when we can do randomization easily and the randomization has more benefits than matching the participants?

Honestly, I search for the answer but I couldn't find any, and obviously that is why I'm asking a question, yet if you find any alike question I would be happy if you refer me to it. I genuinely appreciate it if you refer me to at least one resource as well. The reference book for the discrimination between these two designs: Introduction to Research Methods and Data Analysis in Psychology, Third Edition by Darren Langdridge and Gareth Hagger-Johnson

• experiment-design

The first paper I found searching for "advantages of quasi-experimental design" was this one:

Schweizer, M. L., Braun, B. I., & Milstone, A. M. (2016). Research methods in healthcare epidemiology and antimicrobial stewardship—quasi-experimental designs. Infection control & hospital epidemiology, 37(10), 1135-1140.

Most of the benefits are pragmatic: less cost, potential for retrospective analysis, bypassing ethical considerations that present barriers to randomized trials, etc.

An example of the type of quasi-randomized design I've often been involved in myself is when the data have already been collected in normal medical practice. Sometimes these patients are difficult if not impossible to consent: an intensive-care unit population, for example. Those patients are very sick and their imminent needs are live-saving care; there may not be time to obtain consent for a randomized trial. However, if practices and policies change over time or are different in different facilities, you can use a quasi-experimental design to determine whether those changes or differences in standard of care have an important impact or not.

• 1 $\begingroup$ Thank you very much Bryan Krause! your response was really helpful. what exceptionally grabbed my attention in your answer was ethical problems of randomization and it intrigued me to do more search about it. So, I found out that one of its ethical problems is that some people expect to be benefited from the intervention, but by doing so they might miss the chance( according to link . Now I'm wondering whether that is the solely ethical consideration for randomization, and it will be nice of you if you reply to this question too. $\endgroup$ –  Ali Sirous Commented Apr 17, 2020 at 19:49
• 2 $\begingroup$ @AliSirous That's one case - I talked about that a bit in my answer. Let's say there is a change in standard of care, and we assume the new one is better. It may not be ethical to randomize people to the old standard of care. But, maybe the change was made based on limited data. We could design a large study where we compare outcomes before the change to outcomes after : this is a quasi-experiment that doesn't expose anyone to study-associated risk, and can be conducted without even getting patient consent after IRB approval. $\endgroup$ –  Bryan Krause ♦ Commented Apr 17, 2020 at 20:36
• $\begingroup$ thank you very much again. Now, I comprehend it substantially better. $\endgroup$ –  Ali Sirous Commented Apr 18, 2020 at 5:01

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Quasi-experimental designs for causal inference: an overview

• Published: 26 June 2024

Cite this article

• Heining Cham   ORCID: orcid.org/0000-0002-2933-056X 1 ,
• Hyunjung Lee 1 &
• Igor Migunov 1  

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The randomized control trial (RCT) is the primary experimental design in education research due to its strong internal validity for causal inference. However, in situations where RCTs are not feasible or ethical, quasi-experiments are alternatives to establish causal inference. This paper serves as an introduction to several quasi-experimental designs: regression discontinuity design, difference-in-differences analysis, interrupted time series design, instrumental variable analysis, and propensity score analysis with examples in education research.

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Understanding the Complexities of Experimental Analysis in the Context of Higher Education

Defining, identifying, and estimating causal effects with the potential outcomes framework: a review for education research

The search engine by EBSCO does not offer searches within the publications’ keywords. We replicated the same search in PsycINFO, and its search engine allows searches within the publications’ keywords. The results from PsycINFO were, in general, consistent with the results from ERIC and are available upon request.

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Acknowledgements

This research was supported by a R01 grant from the National Institute on Aging (NIA) (R01AG065110), R01 grants from the National Institute on Minority Health and Health Disparities (R01MD015763 and R01MD015715), and a R21 grant from the National Institute of Mental Health (R21MH124902). The content is solely the responsibility of the authors and does not necessarily represent the official views of the National Institute on Aging, National Institute on Minority Health and Health Disparities, or the National Institute of Mental Health. We thank Dr. Peter M. Steiner, Dr. Yongnam Kim, and the anonymous reviewers for their valuable comments and suggestions on the earlier draft of this paper.

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Cham, H., Lee, H. & Migunov, I. Quasi-experimental designs for causal inference: an overview. Asia Pacific Educ. Rev. (2024). https://doi.org/10.1007/s12564-024-09981-2

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DOI : https://doi.org/10.1007/s12564-024-09981-2

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