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Quasi-Experimental Design | Definition, Types & Examples

Quasi-Experimental Design | Definition, Types & Examples

Published on July 31, 2020 by Lauren Thomas . Revised on January 22, 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.

Quasi-experimental design vs. experimental design

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

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

	True experimental design	Quasi-experimental design
Assignment to treatment	The researcher subjects to control and treatment groups.	Some other, method is used to assign subjects to groups.
Control over treatment	The researcher usually .	The researcher often , but instead studies pre-existing groups that received different treatments after the fact.
Use of	Requires the use of .	Control groups are not required (although they are commonly used).

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 randomization, 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.

If you want to know more about statistics , methodology , or research bias , make sure to check out some of our other articles with explanations and examples.

Normal distribution
Degrees of freedom
Null hypothesis
Discourse analysis
Control groups
Mixed methods research
Non-probability sampling
Quantitative research
Ecological validity

Research bias

Rosenthal effect
Implicit bias
Cognitive bias
Selection bias
Negativity bias
Status quo bias

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.

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.

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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Quasi Experimental Design Overview & Examples

By Jim Frost Leave a Comment

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.

Image illustrating a quasi experimental design.

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.

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

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

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.

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> The Cambridge Handbook of Research Methods and Statistics for the Social and Behavioral Sciences
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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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A Modern Guide to Understanding and Conducting Research in Psychology

Chapter 7 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 et al., 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, focusing first on nonequivalent groups, pretest-posttest, interrupted time series, and combination designs before turning to single subject designs (including reversal and multiple-baseline designs).

7.1 Nonequivalent Groups Design

7.2 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 STEM education program on elementary school students’ attitudes toward science, technology, engineering and math. The researcher could measure the attitudes of students at a particular elementary school during one week, implement the STEM 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 science program aired on television and many of the students watched it, or perhaps a major scientific discover occured 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 more exposed to STEM subjects in class 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.

Finally, it is possible that the act of taking a pretest can sensitize participants to the measurement process or heighten their awareness of the variable under investigation. This heightened sensitivity, called a testing effect , can subsequently lead to changes in their posttest responses, even in the absence of any external intervention effect.

7.3 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 a recent COVID-19 study, the intervention involved the implementation of state-issued mask mandates and restrictions on on-premises restaurant dining. The researchers examined the impact of these measures on COVID-19 cases and deaths ( Guy Jr et al., 2021 ) . Since there was a rapid reduction in daily case and death growth rates following the implementation of mask mandates, and this effect persisted for an extended period, the researchers concluded that the implementation of mask mandates was the cause of the decrease in COVID-19 transmission. This study employed an interrupted time series design, similar to a pretest-posttest design, as it involved measuring the outcomes before and after the intervention. However, unlike the pretest-posttest design, it incorporated multiple measurements before and after the intervention, providing a more comprehensive analysis of the policy impacts.

Figure 7.1 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 7.1 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 7.1 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.

Two line graphs. The x-axes on both are labeled Week and range from 0 to 14. The y-axes on both are labeled Absences and range from 0 to 8. Between weeks 7 and 8 a vertical dotted line indicates when a treatment was introduced. Both graphs show generally high levels of absences from weeks 1 through 7 (before the treatment) and only 2 absences in week 8 (the first observation after the treatment). The top graph shows the absence level staying low from weeks 9 to 14. The bottom graph shows the absence level for weeks 9 to 15 bouncing around at the same high levels as before the treatment.

Figure 7.1: 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.

7.4 Combination Designs

Imagine, for example, that students in one school are given a pretest on their current level of engagement in pro-environmental behaviors (i.e., recycling, eating less red meat, abstaining for single-use plastics, etc.), then are exposed to an pro-environmental program in which they learn about the effects of human caused climate change on the planet, and finally are given a posttest. Students in a similar school are given the pretest, not exposed to an pro-environmental program, and finally are given a posttest. Again, if students in the treatment condition become more involved in pro-environmental behaviors, 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 engage in more pro-environmental behaviors than students in the control condition. But if it is a matter of history (e.g., news of a forest fire or drought) or maturation (e.g., improved reasoning or sense of responsibility), 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 local heat wave with record high temperatures), 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, this kind of design 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.

regression to the mean

Spontaneous remission, 7.5 single-subject research.

Explain what single-subject research is, including how it differs from other types of psychological research and who uses single-subject research and why.
Design simple single-subject studies using reversal and multiple-baseline designs.
Explain how single-subject research designs address the issue of internal validity.
Interpret the results of simple single-subject studies based on the visual inspection of graphed data.
Explain some of the points of disagreement between advocates of single-subject research and advocates of group research.

Researcher Vance Hall and his colleagues were faced with the challenge of increasing the extent to which six disruptive elementary school students stayed focused on their schoolwork ( Hall et al., 1968 ) . For each of several days, the researchers carefully recorded whether or not each student was doing schoolwork every 10 seconds during a 30-minute period. Once they had established this baseline, they introduced a treatment. The treatment was that when the student was doing schoolwork, the teacher gave him or her positive attention in the form of a comment like “good work” or a pat on the shoulder. The result was that all of the students dramatically increased their time spent on schoolwork and decreased their disruptive behavior during this treatment phase. For example, a student named Robbie originally spent 25% of his time on schoolwork and the other 75% “snapping rubber bands, playing with toys from his pocket, and talking and laughing with peers” (p. 3). During the treatment phase, however, he spent 71% of his time on schoolwork and only 29% on other activities. Finally, when the researchers had the teacher stop giving positive attention, the students all decreased their studying and increased their disruptive behavior. This was consistent with the claim that it was, in fact, the positive attention that was responsible for the increase in studying. This was one of the first studies to show that attending to positive behavior—and ignoring negative behavior—could be a quick and effective way to deal with problem behavior in an applied setting.

Single-subject research has shown that positive attention from a teacher for studying can increase studying and decrease disruptive behavior. *Photo by Jerry Wang on Unsplash.*

Figure 7.2: Single-subject research has shown that positive attention from a teacher for studying can increase studying and decrease disruptive behavior. Photo by Jerry Wang on Unsplash.

Most of this book is about what can be called group research, which typically involves studying a large number of participants and combining their data to draw general conclusions about human behavior. The study by Hall and his colleagues, in contrast, is an example of single-subject research, which typically involves studying a small number of participants and focusing closely on each individual. In this section, we consider this alternative approach. We begin with an overview of single-subject research, including some assumptions on which it is based, who conducts it, and why they do. We then look at some basic single-subject research designs and how the data from those designs are analyzed. Finally, we consider some of the strengths and weaknesses of single-subject research as compared with group research and see how these two approaches can complement each other.

Overview of Single-Subject Research

What is single-subject research.

Single-subject research is a type of quantitative, quasi-experimental research that involves studying in detail the behavior of each of a small number of participants. Note that the term single-subject does not mean that only one participant is studied; it is more typical for there to be somewhere between two and 10 participants. (This is why single-subject research designs are sometimes called small-n designs, where n is the statistical symbol for the sample size.) Single-subject research can be contrasted with group research , which typically involves studying large numbers of participants and examining their behavior primarily in terms of group means, standard deviations, and so on. The majority of this book is devoted to understanding group research, which is the most common approach in psychology. But single-subject research is an important alternative, and it is the primary approach in some areas of psychology.

Before continuing, it is important to distinguish single-subject research from two other approaches, both of which involve studying in detail a small number of participants. One is qualitative research, which focuses on understanding people’s subjective experience by collecting relatively unstructured data (e.g., detailed interviews) and analyzing those data using narrative rather than quantitative techniques (see. Single-subject research, in contrast, focuses on understanding objective behavior through experimental manipulation and control, collecting highly structured data, and analyzing those data quantitatively.

It is also important to distinguish single-subject research from case studies. A case study is a detailed description of an individual, which can include both qualitative and quantitative analyses. (Case studies that include only qualitative analyses can be considered a type of qualitative research.) The history of psychology is filled with influential cases studies, such as Sigmund Freud’s description of “Anna O.” (see box “The Case of ‘Anna O.’”) and John Watson and Rosalie Rayner’s description of Little Albert ( Watson & Rayner, 1920 ) who learned to fear a white rat—along with other furry objects—when the researchers made a loud noise while he was playing with the rat. Case studies can be useful for suggesting new research questions and for illustrating general principles. They can also help researchers understand rare phenomena, such as the effects of damage to a specific part of the human brain. As a general rule, however, case studies cannot substitute for carefully designed group or single-subject research studies. One reason is that case studies usually do not allow researchers to determine whether specific events are causally related, or even related at all. For example, if a patient is described in a case study as having been sexually abused as a child and then as having developed an eating disorder as a teenager, there is no way to determine whether these two events had anything to do with each other. A second reason is that an individual case can always be unusual in some way and therefore be unrepresentative of people more generally. Thus case studies have serious problems with both internal and external validity.

The Case of “Anna O.”

Sigmund Freud used the case of a young woman he called “Anna O.” to illustrate many principles of his theory of psychoanalysis ( Freud, 1957 ) . (Her real name was Bertha Pappenheim, and she was an early feminist who went on to make important contributions to the field of social work.) Anna had come to Freud’s colleague Josef Breuer around 1880 with a variety of odd physical and psychological symptoms. One of them was that for several weeks she was unable to drink any fluids. According to Freud,

She would take up the glass of water that she longed for, but as soon as it touched her lips she would push it away like someone suffering from hydrophobia.…She lived only on fruit, such as melons, etc., so as to lessen her tormenting thirst (p. 9).

But according to Freud, a breakthrough came one day while Anna was under hypnosis.

[S]he grumbled about her English “lady-companion,” whom she did not care for, and went on to describe, with every sign of disgust, how she had once gone into this lady’s room and how her little dog—horrid creature!—had drunk out of a glass there. The patient had said nothing, as she had wanted to be polite. After giving further energetic expression to the anger she had held back, she asked for something to drink, drank a large quantity of water without any difficulty, and awoke from her hypnosis with the glass at her lips; and thereupon the disturbance vanished, never to return.

Freud’s interpretation was that Anna had repressed the memory of this incident along with the emotion that it triggered and that this was what had caused her inability to drink. Furthermore, her recollection of the incident, along with her expression of the emotion she had repressed, caused the symptom to go away.

As an illustration of Freud’s theory, the case study of Anna O. is quite effective. As evidence for the theory, however, it is essentially worthless. The description provides no way of knowing whether Anna had really repressed the memory of the dog drinking from the glass, whether this repression had caused her inability to drink, or whether recalling this “trauma” relieved the symptom. It is also unclear from this case study how typical or atypical Anna’s experience was.

Figure 7.3: “Anna O.” was the subject of a famous case study used by Freud to illustrate the principles of psychoanalysis. Source: Wikimedia Commons

Assumptions of Single-Subject Research

Again, single-subject research involves studying a small number of participants and focusing intensively on the behavior of each one. But why take this approach instead of the group approach? There are two important assumptions underlying single-subject research, and it will help to consider them now.

First and foremost is the assumption that it is important to focus intensively on the behavior of individual participants. One reason for this is that group research can hide individual differences and generate results that do not represent the behavior of any individual. For example, a treatment that has a positive effect for half the people exposed to it but a negative effect for the other half would, on average, appear to have no effect at all. Single-subject research, however, would likely reveal these individual differences. A second reason to focus intensively on individuals is that sometimes it is the behavior of a particular individual that is primarily of interest. A school psychologist, for example, might be interested in changing the behavior of a particular disruptive student. Although previous published research (both single-subject and group research) is likely to provide some guidance on how to do this, conducting a study on this student would be more direct and probably more effective.

Another assumption of single-subject research is that it is important to study strong and consistent effects that have biological or social importance. Applied researchers, in particular, are interested in treatments that have substantial effects on important behaviors and that can be implemented reliably in the real-world contexts in which they occur. This is sometimes referred to as social validity ( Wolf, 1978 ) . The study by Hall and his colleagues, for example, had good social validity because it showed strong and consistent effects of positive teacher attention on a behavior that is of obvious importance to teachers, parents, and students. Furthermore, the teachers found the treatment easy to implement, even in their often chaotic elementary school classrooms.

Who Uses Single-Subject Research?

Single-subject research has been around as long as the field of psychology itself. In the late 1800s, one of psychology’s founders, Wilhelm Wundt, studied sensation and consciousness by focusing intensively on each of a small number of research participants. Herman Ebbinghaus’s research on memory and Ivan Pavlov’s research on classical conditioning are other early examples, both of which are still described in almost every introductory psychology textbook.

In the middle of the 20th century, B. F. Skinner clarified many of the assumptions underlying single-subject research and refined many of its techniques ( Skinner, 1938 ) . He and other researchers then used it to describe how rewards, punishments, and other external factors affect behavior over time. This work was carried out primarily using nonhuman subjects—mostly rats and pigeons. This approach, which Skinner called the experimental analysis of behavior —remains an important subfield of psychology and continues to rely almost exclusively on single-subject research. For examples of this work, look at any issue of the Journal of the Experimental Analysis of Behavior . By the 1960s, many researchers were interested in using this approach to conduct applied research primarily with humans—a subfield now called applied behavior analysis ( Baer et al., 1968 ) . Applied behavior analysis plays a significant role in contemporary research on developmental disabilities, education, organizational behavior, and health, among many other areas. Examples of this work (including the study by Hall and his colleagues) can be found in the Journal of Applied Behavior Analysis . The single-subject approach can also be used by clinicians who take any theoretical perspective—behavioral, cognitive, psychodynamic, or humanistic—to study processes of therapeutic change with individual clients and to document their clients’ improvement ( Kazdin, 2019 ) .

Single-Subject Research Designs

General features of single-subject designs.

Before looking at any specific single-subject research designs, it will be helpful to consider some features that are common to most of them. Many of these features are illustrated in Figure 7.4 , which shows the results of a generic single-subject study. First, the dependent variable (represented on the y-axis of the graph) is measured repeatedly over time (represented by the x-axis) at regular intervals. Second, the study is divided into distinct phases, and the participant is tested under one condition per phase. The conditions are often designated by capital letters: A, B, C, and so on. Thus Figure 7.4 represents a design in which the participant was tested first in one condition (A), then tested in another condition (B), and finally retested in the original condition (A). (This is called a reversal design and will be discussed in more detail shortly.)

Figure 7.4: Results of a generic single-subject study illustrating several principles of single-subject research.

Another important aspect of single-subject research is that the change from one condition to the next does not usually occur after a fixed amount of time or number of observations. Instead, it depends on the participant’s behavior. Specifically, the researcher waits until the participant’s behavior in one condition becomes fairly consistent from observation to observation before changing conditions. This is sometimes referred to as the steady state strategy ( Sidman, 1960 ) . The idea is that when the dependent variable has reached a steady state, then any change across conditions will be relatively easy to detect. Recall that we encountered this same principle when discussing experimental research more generally. The effect of an independent variable is easier to detect when the “noise” in the data is minimized.

Reversal Designs

The most basic single-subject research design is the reversal design , also called the ABA design . During the first phase, A, a baseline is established for the dependent variable. This is the level of responding before any treatment is introduced, and therefore the baseline phase is a kind of control condition. When steady state responding is reached, phase B begins as the researcher introduces the treatment. Again, the researcher waits until that dependent variable reaches a steady state so that it is clear whether and how much it has changed. Finally, the researcher removes the treatment and again waits until the dependent variable reaches a steady state. This basic reversal design can also be extended with the reintroduction of the treatment (ABAB), another return to baseline (ABABA), and so on. The study by Hall and his colleagues was an ABAB reversal design (Figure 7.5 ).

An approximation of the results for Hall and colleagues’ participant Robbie in their ABAB reversal design. The percentage of time he spent studying (the dependent variable) was low during the first baseline phase, increased during the first treatment phase until it leveled off, decreased during the second baseline phase, and again increased during the second treatment phase.

Figure 7.5: An approximation of the results for Hall and colleagues’ participant Robbie in their ABAB reversal design. The percentage of time he spent studying (the dependent variable) was low during the first baseline phase, increased during the first treatment phase until it leveled off, decreased during the second baseline phase, and again increased during the second treatment phase.

Why is the reversal—the removal of the treatment—considered to be necessary in this type of design? If the dependent variable changes after the treatment is introduced, it is not always clear that the treatment was responsible for the change. It is possible that something else changed at around the same time and that this extraneous variable is responsible for the change in the dependent variable. But if the dependent variable changes with the introduction of the treatment and then changes back with the removal of the treatment, it is much clearer that the treatment (and removal of the treatment) is the cause. In other words, the reversal greatly increases the internal validity of the study.

Multiple-Baseline Designs

There are two potential problems with the reversal design—both of which have to do with the removal of the treatment. One is that if a treatment is working, it may be unethical to remove it. For example, if a treatment seemed to reduce the incidence of self-injury in a developmentally disabled child, it would be unethical to remove that treatment just to show that the incidence of self-injury increases. The second problem is that the dependent variable may not return to baseline when the treatment is removed. For example, when positive attention for studying is removed, a student might continue to study at an increased rate. This could mean that the positive attention had a lasting effect on the student’s studying, which of course would be good, but it could also mean that the positive attention was not really the cause of the increased studying in the first place.

One solution to these problems is to use a multiple-baseline design , which is represented in Figure 7.6 . In one version of the design, a baseline is established for each of several participants, and the treatment is then introduced for each one. In essence, each participant is tested in an AB design. The key to this design is that the treatment is introduced at a different time for each participant. The idea is that if the dependent variable changes when the treatment is introduced for one participant, it might be a coincidence. But if the dependent variable changes when the treatment is introduced for multiple participants—especially when the treatment is introduced at different times for the different participants—then it is less likely to be a coincidence.

Results of a generic multiple-baseline study. The multiple baselines can be for different participants, dependent variables, or settings. The treatment is introduced at a different time on each baseline.

Figure 7.6: Results of a generic multiple-baseline study. The multiple baselines can be for different participants, dependent variables, or settings. The treatment is introduced at a different time on each baseline.

As an example, consider a study by Scott Ross and Robert Horner ( Ross et al., 2009 ) . They were interested in how a school-wide bullying prevention program affected the bullying behavior of particular problem students. At each of three different schools, the researchers studied two students who had regularly engaged in bullying. During the baseline phase, they observed the students for 10-minute periods each day during lunch recess and counted the number of aggressive behaviors they exhibited toward their peers. (The researchers used handheld computers to help record the data.) After 2 weeks, they implemented the program at one school. After 2 more weeks, they implemented it at the second school. And after 2 more weeks, they implemented it at the third school. They found that the number of aggressive behaviors exhibited by each student dropped shortly after the program was implemented at his or her school. Notice that if the researchers had only studied one school or if they had introduced the treatment at the same time at all three schools, then it would be unclear whether the reduction in aggressive behaviors was due to the bullying program or something else that happened at about the same time it was introduced (e.g., a holiday, a television program, a change in the weather). But with their multiple-baseline design, this kind of coincidence would have to happen three separate times—an unlikely occurrence—to explain their results.

Data Analysis in Single-Subject Research

In addition to its focus on individual participants, single-subject research differs from group research in the way the data are typically analyzed. As we have seen throughout the book, group research involves combining data across participants. Inferential statistics are used to help decide whether the result for the sample is likely to generalize to the population. Single-subject research, by contrast, relies heavily on a very different approach called visual inspection . This means plotting individual participants’ data as shown throughout this chapter, looking carefully at those data, and making judgments about whether and to what extent the independent variable had an effect on the dependent variable. Inferential statistics are typically not used.

In visually inspecting their data, single-subject researchers take several factors into account. One of them is changes in the level of the dependent variable from condition to condition. If the dependent variable is much higher or much lower in one condition than another, this suggests that the treatment had an effect. A second factor is trend , which refers to gradual increases or decreases in the dependent variable across observations. If the dependent variable begins increasing or decreasing with a change in conditions, then again this suggests that the treatment had an effect. It can be especially telling when a trend changes directions—for example, when an unwanted behavior is increasing during baseline but then begins to decrease with the introduction of the treatment. A third factor is latency , which is the time it takes for the dependent variable to begin changing after a change in conditions. In general, if a change in the dependent variable begins shortly after a change in conditions, this suggests that the treatment was responsible.

In the top panel of Figure 7.7 , there are fairly obvious changes in the level and trend of the dependent variable from condition to condition. Furthermore, the latencies of these changes are short; the change happens immediately. This pattern of results strongly suggests that the treatment was responsible for the changes in the dependent variable. In the bottom panel of Figure 7.7 , however, the changes in level are fairly small. And although there appears to be an increasing trend in the treatment condition, it looks as though it might be a continuation of a trend that had already begun during baseline. This pattern of results strongly suggests that the treatment was not responsible for any changes in the dependent variable—at least not to the extent that single-subject researchers typically hope to see.

Figure 7.7: Visual inspection of the data suggests an effective treatment in the top panel but an ineffective treatment in the bottom panel.

The results of single-subject research can also be analyzed using statistical procedures—and this is becoming more common. There are many different approaches, and single-subject researchers continue to debate which are the most useful. One approach parallels what is typically done in group research. The mean and standard deviation of each participant’s responses under each condition are computed and compared, and inferential statistical tests such as the t test or analysis of variance are applied ( Fisch, 2001 ) . (Note that averaging across participants is less common.) Another approach is to compute the percentage of nonoverlapping data (PND) for each participant ( Scruggs & Mastropieri, 2021 ) . This is the percentage of responses in the treatment condition that are more extreme than the most extreme response in a relevant control condition. In the study of Hall and his colleagues, for example, all measures of Robbie’s study time in the first treatment condition were greater than the highest measure in the first baseline, for a PND of 100%. The greater the percentage of nonoverlapping data, the stronger the treatment effect. Still, formal statistical approaches to data analysis in single-subject research are generally considered a supplement to visual inspection, not a replacement for it.

The Single-Subject Versus Group “Debate”

Single-subject research is similar to group research—especially experimental group research—in many ways. They are both quantitative approaches that try to establish causal relationships by manipulating an independent variable, measuring a dependent variable, and controlling extraneous variables. As we will see, single-subject research and group research are probably best conceptualized as complementary approaches.

Data Analysis

One set of disagreements revolves around the issue of data analysis. Some advocates of group research worry that visual inspection is inadequate for deciding whether and to what extent a treatment has affected a dependent variable. One specific concern is that visual inspection is not sensitive enough to detect weak effects. A second is that visual inspection can be unreliable, with different researchers reaching different conclusions about the same set of data ( Danov & Symons, 2008 ) . A third is that the results of visual inspection—an overall judgment of whether or not a treatment was effective—cannot be clearly and efficiently summarized or compared across studies (unlike the measures of relationship strength typically used in group research).

In general, single-subject researchers share these concerns. However, they also argue that their use of the steady state strategy, combined with their focus on strong and consistent effects, minimizes most of them. If the effect of a treatment is difficult to detect by visual inspection because the effect is weak or the data are noisy, then single-subject researchers look for ways to increase the strength of the effect or reduce the noise in the data by controlling extraneous variables (e.g., by administering the treatment more consistently). If the effect is still difficult to detect, then they are likely to consider it neither strong enough nor consistent enough to be of further interest. Many single-subject researchers also point out that statistical analysis is becoming increasingly common and that many of them are using it as a supplement to visual inspection—especially for the purpose of comparing results across studies ( Scruggs & Mastropieri, 2021 ) .

Turning the tables, some advocates of single-subject research worry about the way that group researchers analyze their data. Specifically, they point out that focusing on group means can be highly misleading. Again, imagine that a treatment has a strong positive effect on half the people exposed to it and an equally strong negative effect on the other half. In a traditional between-subjects experiment, the positive effect on half the participants in the treatment condition would be statistically cancelled out by the negative effect on the other half. The mean for the treatment group would then be the same as the mean for the control group, making it seem as though the treatment had no effect when in fact it had a strong effect on every single participant!

But again, group researchers share this concern. Although they do focus on group statistics, they also emphasize the importance of examining distributions of individual scores. For example, if some participants were positively affected by a treatment and others negatively affected by it, this would produce a bimodal distribution of scores and could be detected by looking at a histogram of the data. The use of within-subjects designs is another strategy that allows group researchers to observe effects at the individual level and even to specify what percentage of individuals exhibit strong, medium, weak, and even negative effects.

External Validity

The second issue about which single-subject and group researchers sometimes disagree has to do with external validity—the ability to generalize the results of a study beyond the people and situation actually studied. In particular, advocates of group research point out the difficulty in knowing whether results for just a few participants are likely to generalize to others in the population. Imagine, for example, that in a single-subject study, a treatment has been shown to reduce self-injury for each of two developmentally disabled children. Even if the effect is strong for these two children, how can one know whether this treatment is likely to work for other developmentally disabled children?

Again, single-subject researchers share this concern. In response, they note that the strong and consistent effects they are typically interested in—even when observed in small samples—are likely to generalize to others in the population. Single-subject researchers also note that they place a strong emphasis on replicating their research results. When they observe an effect with a small sample of participants, they typically try to replicate it with another small sample—perhaps with a slightly different type of participant or under slightly different conditions. Each time they observe similar results, they rightfully become more confident in the generality of those results. Single-subject researchers can also point to the fact that the principles of classical and operant conditioning—most of which were discovered using the single-subject approach—have been successfully generalized across an incredibly wide range of species and situations.

And again turning the tables, single-subject researchers have concerns of their own about the external validity of group research. One extremely important point they make is that studying large groups of participants does not entirely solve the problem of generalizing to other individuals. Imagine, for example, a treatment that has been shown to have a small positive effect on average in a large group study. It is likely that although many participants exhibited a small positive effect, others exhibited a large positive effect, and still others exhibited a small negative effect. When it comes to applying this treatment to another large group , we can be fairly sure that it will have a small effect on average. But when it comes to applying this treatment to another individual , we cannot be sure whether it will have a small, a large, or even a negative effect. Another point that single-subject researchers make is that group researchers also face a similar problem when they study a single situation and then generalize their results to other situations. For example, researchers who conduct a study on the effect of cell phone use on drivers on a closed oval track probably want to apply their results to drivers in many other real-world driving situations. But notice that this requires generalizing from a single situation to a population of situations. Thus the ability to generalize is based on much more than just the sheer number of participants one has studied. It requires a careful consideration of the similarity of the participants and situations studied to the population of participants and situations that one wants to generalize to ( Shadish et al., 2002 ) .

Single-Subject and Group Research as Complementary Methods

As with quantitative and qualitative research, it is probably best to conceptualize single-subject research and group research as complementary methods that have different strengths and weaknesses and that are appropriate for answering different kinds of research questions ( Kazdin, 2019 ) . Single-subject research is particularly good for testing the effectiveness of treatments on individuals when the focus is on strong, consistent, and biologically or socially important effects. It is especially useful when the behavior of particular individuals is of interest. Clinicians who work with only one individual at a time may find that it is their only option for doing systematic quantitative research.

Group research, on the other hand, is good for testing the effectiveness of treatments at the group level. Among the advantages of this approach is that it allows researchers to detect weak effects, which can be of interest for many reasons. For example, finding a weak treatment effect might lead to refinements of the treatment that eventually produce a larger and more meaningful effect. Group research is also good for studying interactions between treatments and participant characteristics. For example, if a treatment is effective for those who are high in motivation to change and ineffective for those who are low in motivation to change, then a group design can detect this much more efficiently than a single-subject design. Group research is also necessary to answer questions that cannot be addressed using the single-subject approach, including questions about independent variables that cannot be manipulated (e.g., number of siblings, extroversion, culture).

Single-subject research—which involves testing a small number of participants and focusing intensively on the behavior of each individual—is an important alternative to group research in psychology.
Single-subject studies must be distinguished from case studies, in which an individual case is described in detail. Case studies can be useful for generating new research questions, for studying rare phenomena, and for illustrating general principles. However, they cannot substitute for carefully controlled experimental or correlational studies because they are low in internal and external validity.
Single-subject research designs typically involve measuring the dependent variable repeatedly over time and changing conditions (e.g., from baseline to treatment) when the dependent variable has reached a steady state. This approach allows the researcher to see whether changes in the independent variable are causing changes in the dependent variable.
Single-subject researchers typically analyze their data by graphing them and making judgments about whether the independent variable is affecting the dependent variable based on level, trend, and latency.
Differences between single-subject research and group research sometimes lead to disagreements between single-subject and group researchers. These disagreements center on the issues of data analysis and external validity (especially generalization to other people). Single-subject research and group research are probably best seen as complementary methods, with different strengths and weaknesses, that are appropriate for answering different kinds of research questions.
Does positive attention from a parent increase a child’s toothbrushing behavior?
Does self-testing while studying improve a student’s performance on weekly spelling tests?
Does regular exercise help relieve depression?
Practice: Create a graph that displays the hypothetical results for the study you designed in Exercise 1. Write a paragraph in which you describe what the results show. Be sure to comment on level, trend, and latency.
Discussion: Imagine you have conducted a single-subject study showing a positive effect of a treatment on the behavior of a man with social anxiety disorder. Your research has been criticized on the grounds that it cannot be generalized to others. How could you respond to this criticism?
Discussion: Imagine you have conducted a group study showing a positive effect of a treatment on the behavior of a group of people with social anxiety disorder, but your research has been criticized on the grounds that “average” effects cannot be generalized to individuals. How could you respond to this criticism?

7.6 Glossary

The simplest reversal design, in which there is a baseline condition (A), followed by a treatment condition (B), followed by a return to baseline (A).

applied behavior analysis

A subfield of psychology that uses single-subject research and applies the principles of behavior analysis to real-world problems in areas that include education, developmental disabilities, organizational behavior, and health behavior.

A condition in a single-subject research design in which the dependent variable is measured repeatedly in the absence of any treatment. Most designs begin with a baseline condition, and many return to the baseline condition at least once.

A detailed description of an individual case.

experimental analysis of behavior

A subfield of psychology founded by B. F. Skinner that uses single-subject research—often with nonhuman animals—to study relationships primarily between environmental conditions and objectively observable behaviors.

group research

A type of quantitative research that involves studying a large number of participants and examining their behavior in terms of means, standard deviations, and other group-level statistics.

interrupted time-series design

A research design in which a series of measurements of the dependent variable are taken both before and after a treatment.

item-order effect

The effect of responding to one survey item on responses to a later survey item.

Refers collectively to extraneous developmental changes in participants that can occur between a pretest and posttest or between the first and last measurements in a time series. It can provide an alternative explanation for an observed change in the dependent variable.

multiple-baseline design

A single-subject research design in which multiple baselines are established for different participants, different dependent variables, or different contexts and the treatment is introduced at a different time for each baseline.

naturalistic observation

An approach to data collection in which the behavior of interest is observed in the environment in which it typically occurs.

nonequivalent groups design

A between-subjects research design in which participants are not randomly assigned to conditions, usually because participants are in preexisting groups (e.g., students at different schools).

nonexperimental research

Research that lacks the manipulation of an independent variable or the random assignment of participants to conditions or orders of conditions.

open-ended item

A questionnaire item that asks a question and allows respondents to respond in whatever way they want.

percentage of nonoverlapping data

A statistic sometimes used in single-subject research. The percentage of observations in a treatment condition that are more extreme than the most extreme observation in a relevant baseline condition.

pretest-posttest design

A research design in which the dependent variable is measured (the pretest), a treatment is given, and the dependent variable is measured again (the posttest) to see if there is a change in the dependent variable from pretest to posttest.

quasi-experimental research

Research that involves the manipulation of an independent variable but lacks the random assignment of participants to conditions or orders of conditions. It is generally used in field settings to test the effectiveness of a treatment.

rating scale

An ordered set of response options to a closed-ended questionnaire item.

The statistical fact that an individual who scores extremely on one occasion will tend to score less extremely on the next occasion.

A term often used to refer to a participant in survey research.

reversal design

A single-subject research design that begins with a baseline condition with no treatment, followed by the introduction of a treatment, and after that a return to the baseline condition. It can include additional treatment conditions and returns to baseline.

single-subject research

A type of quantitative research that involves examining in detail the behavior of each of a small number of participants.

single-variable research

Research that focuses on a single variable rather than on a statistical relationship between variables.

social validity

The extent to which a single-subject study focuses on an intervention that has a substantial effect on an important behavior and can be implemented reliably in the real-world contexts (e.g., by teachers in a classroom) in which that behavior occurs.

Improvement in a psychological or medical problem over time without any treatment.

steady state strategy

In single-subject research, allowing behavior to become fairly consistent from one observation to the next before changing conditions. This makes any effect of the treatment easier to detect.

survey research

A quantitative research approach that uses self-report measures and large, carefully selected samples.

testing effect

A bias in participants’ responses in which scores on the posttest are influenced by simple exposure to the pretest

visual inspection

The primary approach to data analysis in single-subject research, which involves graphing the data and making a judgment as to whether and to what extent the independent variable affected the dependent variable.

The use and interpretation of quasi-experimental design

Last updated

6 February 2023

Reviewed by

Miroslav Damyanov

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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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Quasi-experimental study designs series-paper 4: uses and value

Affiliations.

1 Institute of Public Health, Faculty of Medicine, Heidelberg University, Heidelberg, Germany; Department of Global Health and Population, Harvard T.H. Chan School of Public Health, Boston, USA; Africa Health Research Institute, Somkhele, South Africa. Electronic address: [email protected].
2 Department of Medicine, University of Ottawa, Ottawa, Canada.
3 Department of Health Management and Health Economics, University of Oslo, Oslo, Norway.
4 Institute of Education, University College London, London, UK.
5 Center for Global Health and Development, Boston University, Boston, USA.
6 Department of Global Health and Population, Harvard T.H. Chan School of Public Health, Boston, USA.
7 Department of Global Health and Population, Harvard T.H. Chan School of Public Health, Boston, USA; Department of Health Research Methods, Evidence and Impact, Centre for Health Economics and Policy Analysis, McMaster Health Forum, Hamilton, Ontario, Canada; Department of Political Science, McMaster University, Hamilton, Ontario, Canada.
8 Department of Medicine, University of Ottawa, Ottawa, Ontario, Canada.
9 Health Systems Research Unit, South African Medical Research Council, Tygerberg, South Africa.
10 Research and Evaluation Strategic Initiative, FHI360, Washington DC, USA.
11 School of Public Health, Boston University, Boston, USA.
12 Impact Evaluation, World Bank, Washington DC, USA.
13 Department of Information, Evidence and Research, World Health Organization, Geneva, Switzerland.
14 Instituto de Saúde Coletiva, Federal University of Bahia, Salvador, Brazil; National Institute in Science, Technology and Innovation in Health (CITECS), Salvador, Brazil.
15 Department of Economics, University of Göttingen, Göttingen, Germany.
PMID: 28365303
DOI: 10.1016/j.jclinepi.2017.03.012

Quasi-experimental studies are increasingly used to establish causal relationships in epidemiology and health systems research. Quasi-experimental studies offer important opportunities to increase and improve evidence on causal effects: (1) they can generate causal evidence when randomized controlled trials are impossible; (2) they typically generate causal evidence with a high degree of external validity; (3) they avoid the threats to internal validity that arise when participants in nonblinded experiments change their behavior in response to the experimental assignment to either intervention or control arm (such as compensatory rivalry or resentful demoralization); (4) they are often well suited to generate causal evidence on long-term health outcomes of an intervention, as well as nonhealth outcomes such as economic and social consequences; and (5) they can often generate evidence faster and at lower cost than experiments and other intervention studies.

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Research Methodologies Guide

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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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Quasi-experimental Research: What It Is, Types & Examples

quasi-experimental research is research that appears to be experimental but is not.

Much like an actual experiment, quasi-experimental research tries to demonstrate a cause-and-effect link between a dependent and an independent variable. A quasi-experiment, on the other hand, does not depend on random assignment, unlike an actual experiment. The subjects are sorted into groups based on non-random variables.

What is Quasi-Experimental Research?

“Resemblance” is the definition of “quasi.” Individuals are not randomly allocated to conditions or orders of conditions, even though the regression analysis is changed. As a result, quasi-experimental research is research that appears to be experimental but is not.

The directionality problem is avoided in quasi-experimental research since the regression analysis is altered before the multiple regression is assessed. However, because individuals are not randomized at random, there are likely to be additional disparities across conditions in quasi-experimental research.

As a result, in terms of internal consistency, quasi-experiments fall somewhere between correlational research and actual experiments.

The key component of a true experiment is randomly allocated groups. This means that each person has an equivalent chance of being assigned to the experimental group or the control group, depending on whether they are manipulated or not.

Simply put, a quasi-experiment is not a real experiment. A quasi-experiment does not feature randomly allocated groups since the main component of a real experiment is randomly assigned groups. Why is it so crucial to have randomly allocated groups, given that they constitute the only distinction between quasi-experimental and actual experimental research ?

Let’s use an example to illustrate our point. Let’s assume we want to discover how new psychological therapy affects depressed patients. In a genuine trial, you’d split half of the psych ward into treatment groups, With half getting the new psychotherapy therapy and the other half receiving standard depression treatment .

And the physicians compare the outcomes of this treatment to the results of standard treatments to see if this treatment is more effective. Doctors, on the other hand, are unlikely to agree with this genuine experiment since they believe it is unethical to treat one group while leaving another untreated.

A quasi-experimental study will be useful in this case. Instead of allocating these patients at random, you uncover pre-existing psychotherapist groups in the hospitals. Clearly, there’ll be counselors who are eager to undertake these trials as well as others who prefer to stick to the old ways.

These pre-existing groups can be used to compare the symptom development of individuals who received the novel therapy with those who received the normal course of treatment, even though the groups weren’t chosen at random.

If any substantial variations between them can be well explained, you may be very assured that any differences are attributable to the treatment but not to other extraneous variables.

As we mentioned before, quasi-experimental research entails manipulating an independent variable by randomly assigning people to conditions or sequences of conditions. Non-equivalent group designs, pretest-posttest designs, and regression discontinuity designs are only a few of the essential types.

What are quasi-experimental research designs?

Quasi-experimental research designs are a type of research design that is similar to experimental designs but doesn’t give full control over the independent variable(s) like true experimental designs do.

In a quasi-experimental design, the researcher changes or watches an independent variable, but the participants are not put into groups at random. Instead, people are put into groups based on things they already have in common, like their age, gender, or how many times they have seen a certain stimulus.

Because the assignments are not random, it is harder to draw conclusions about cause and effect than in a real experiment. However, quasi-experimental designs are still useful when randomization is not possible or ethical.

The true experimental design may be impossible to accomplish or just too expensive, especially for researchers with few resources. Quasi-experimental designs enable you to investigate an issue by utilizing data that has already been paid for or gathered by others (often the government).

Because they allow better control for confounding variables than other forms of studies, they have higher external validity than most genuine experiments and higher internal validity (less than true experiments) than other non-experimental research.

Is quasi-experimental research quantitative or qualitative?

Quasi-experimental research is a quantitative research method. It involves numerical data collection and statistical analysis. Quasi-experimental research compares groups with different circumstances or treatments to find cause-and-effect links.

It draws statistical conclusions from quantitative data. Qualitative data can enhance quasi-experimental research by revealing participants’ experiences and opinions, but quantitative data is the method’s foundation.

Quasi-experimental research types

There are many different sorts of quasi-experimental designs. Three of the most popular varieties are described below: Design of non-equivalent groups, Discontinuity in regression, and Natural experiments.

Design of Non-equivalent Groups

Example: design of non-equivalent groups, discontinuity in regression, example: discontinuity in regression, natural experiments, example: natural experiments.

However, because they couldn’t afford to pay everyone who qualified for the program, they had to use a random lottery to distribute slots.

Experts were able to investigate the program’s impact by utilizing enrolled people as a treatment group and those who were qualified but did not play the jackpot as an experimental group.

How QuestionPro helps in quasi-experimental research?

QuestionPro can be a useful tool in quasi-experimental research because it includes features that can assist you in designing and analyzing your research study. Here are some ways in which QuestionPro can help in quasi-experimental research:

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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.

Nonequivalent Groups Design

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.

Pretest-Posttest Design

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

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.

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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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:

	Experimental Study (a.k.a. Randomized Controlled Trial)	Quasi-Experimental Study
Objective	Evaluate the effect of an intervention or a treatment	Evaluate the effect of an intervention or a treatment
How participants get assigned to groups?	Random assignment	Non-random assignment (participants get assigned according to their choosing or that of the researcher)
Is there a control group?	Yes	Not always (although, if present, a control group will provide better evidence for the study results)
Is there any room for confounding?	No (although check for a detailed discussion on post-randomization confounding in randomized controlled trials)	Yes (however, statistical techniques can be used to study causal relationships in quasi-experiments)
Level of evidence	A randomized trial is at the highest level in the hierarchy of evidence	A quasi-experiment is one level below the experimental study in the hierarchy of evidence [ ]
Advantages	Minimizes bias and confounding	– Can be used in situations where an experiment is not ethically or practically feasible – Can work with smaller sample sizes than randomized trials
Limitations	– High cost (as it generally requires a large sample size) – Ethical limitations – Generalizability issues – Sometimes practically infeasible	Lower ranking in the hierarchy of evidence as losing the power of randomization causes the study to be more susceptible to bias and confounding

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).

Critical Appraisal Resources for Evidence-Based Nursing Practice

Levels of Evidence
Systematic Reviews
Randomized Controlled Trials
Quasi-Experimental Studies

What is a Quasi-Experimental Study?

Pro tips: quasi-experimental checklist, articles on quasi-experimental design and methodology.

Case-Control Studies
Cohort Studies
Analytical Cross-Sectional Studies
Qualitative Research

E-Books for Terminology and Definitions

Quasi-experimental studies are a type of quantitative research used to investigate the effectiveness of interventions or treatments. These types of studies involve manipulation of the independent variable, yet they lack certain elements of a fully experimental design. Quasi-experimental studies have no random assignment of study subjects and lack a control group (Schmidt & Brown, 2019, p. 177). However, they may have a non-equivalent comparison group (Krishnan, 2019).

Krishnan P. (2019). A review of the non-equivalent control group post-test-only design . Nurse Researcher , 26 (2), 37–40. https://doi.org/10.7748/nr.2018.e1582

Schmidt N. A. & Brown J. M. (2019). Evidence-based practice for nurses: Appraisal and application of research (4th ed.). Jones & Bartlett Learning.

Each JBI Checklist provides tips and guidance on what to look for to answer each question. These tips begin on page 4.

Below are some additional Frequently Asked Questions about the Quasi-Experimental Checklist that have been asked students in previous semesters.


	The 'cause' refers to the independent variable that is being manipulated to observe an 'effect.' The 'effect' is the dependent variable, or the outcome. You will often find this information in the beginning of the study in the objectives/purpose/aim/research question section. Is this information clearly stated? For example: "The purpose of this study is to identify whether mindfulness-based stress reduction ('the cause') reduces anxiety ('the effect') in cancer patients."
	Check for information about the internal reliability or internal consistency of the research instruments (scales, questionnaires, surveys, tools, etc.) used in the study. Look for the Cronbach's alpha statistic which is used to indicate internal reliability of an instrument.

Maciejewski, M. L. (2020). Quasi-experimental design . Biostatistics & Epidemiology , 4(1), 38-47. doi:10.1080/24709360.2018.1477468

Maciejewski, M. L., Curtis, L. H., & Dowd, B. (2013). Study design elements for rigorous quasi-experimental comparative effectiveness research . Journal of Comparative Effectiveness Research , 2 (2), 159–173. https://doi.org/10.2217/cer.13.7

Miller, C. J., Smith, S. N., & Pugatch, M. (2020). Experimental and quasi-experimental designs in implementation research . Psychiatry Research , 283 , 112452. https://doi.org/10.1016/j.psychres.2019.06.027

Siedlecki S. L. (2020). Quasi-experimental research designs . Clinical Nurse Specialist , 34 (5), 198–202. https://doi.org/10.1097/NUR.0000000000000540

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Next: Case-Control Studies >>
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Experimental and Quasi-Experimental Research

Guide Title: Experimental and Quasi-Experimental Research Guide ID: 64

You approach a stainless-steel wall, separated vertically along its middle where two halves meet. After looking to the left, you see two buttons on the wall to the right. You press the top button and it lights up. A soft tone sounds and the two halves of the wall slide apart to reveal a small room. You step into the room. Looking to the left, then to the right, you see a panel of more buttons. You know that you seek a room marked with the numbers 1-0-1-2, so you press the button marked "10." The halves slide shut and enclose you within the cubicle, which jolts upward. Soon, the soft tone sounds again. The door opens again. On the far wall, a sign silently proclaims, "10th floor."

You have engaged in a series of experiments. A ride in an elevator may not seem like an experiment, but it, and each step taken towards its ultimate outcome, are common examples of a search for a causal relationship-which is what experimentation is all about.

You started with the hypothesis that this is in fact an elevator. You proved that you were correct. You then hypothesized that the button to summon the elevator was on the left, which was incorrect, so then you hypothesized it was on the right, and you were correct. You hypothesized that pressing the button marked with the up arrow would not only bring an elevator to you, but that it would be an elevator heading in the up direction. You were right.

As this guide explains, the deliberate process of testing hypotheses and reaching conclusions is an extension of commonplace testing of cause and effect relationships.

Basic Concepts of Experimental and Quasi-Experimental Research

Discovering causal relationships is the key to experimental research. In abstract terms, this means the relationship between a certain action, X, which alone creates the effect Y. For example, turning the volume knob on your stereo clockwise causes the sound to get louder. In addition, you could observe that turning the knob clockwise alone, and nothing else, caused the sound level to increase. You could further conclude that a causal relationship exists between turning the knob clockwise and an increase in volume; not simply because one caused the other, but because you are certain that nothing else caused the effect.

Independent and Dependent Variables

Beyond discovering causal relationships, experimental research further seeks out how much cause will produce how much effect; in technical terms, how the independent variable will affect the dependent variable. You know that turning the knob clockwise will produce a louder noise, but by varying how much you turn it, you see how much sound is produced. On the other hand, you might find that although you turn the knob a great deal, sound doesn't increase dramatically. Or, you might find that turning the knob just a little adds more sound than expected. The amount that you turned the knob is the independent variable, the variable that the researcher controls, and the amount of sound that resulted from turning it is the dependent variable, the change that is caused by the independent variable.

Experimental research also looks into the effects of removing something. For example, if you remove a loud noise from the room, will the person next to you be able to hear you? Or how much noise needs to be removed before that person can hear you?

Treatment and Hypothesis

The term treatment refers to either removing or adding a stimulus in order to measure an effect (such as turning the knob a little or a lot, or reducing the noise level a little or a lot). Experimental researchers want to know how varying levels of treatment will affect what they are studying. As such, researchers often have an idea, or hypothesis, about what effect will occur when they cause something. Few experiments are performed where there is no idea of what will happen. From past experiences in life or from the knowledge we possess in our specific field of study, we know how some actions cause other reactions. Experiments confirm or reconfirm this fact.

Experimentation becomes more complex when the causal relationships they seek aren't as clear as in the stereo knob-turning examples. Questions like "Will olestra cause cancer?" or "Will this new fertilizer help this plant grow better?" present more to consider. For example, any number of things could affect the growth rate of a plant-the temperature, how much water or sun it receives, or how much carbon dioxide is in the air. These variables can affect an experiment's results. An experimenter who wants to show that adding a certain fertilizer will help a plant grow better must ensure that it is the fertilizer, and nothing else, affecting the growth patterns of the plant. To do this, as many of these variables as possible must be controlled.

Matching and Randomization

In the example used in this guide (you'll find the example below), we discuss an experiment that focuses on three groups of plants -- one that is treated with a fertilizer named MegaGro, another group treated with a fertilizer named Plant!, and yet another that is not treated with fetilizer (this latter group serves as a "control" group). In this example, even though the designers of the experiment have tried to remove all extraneous variables, results may appear merely coincidental. Since the goal of the experiment is to prove a causal relationship in which a single variable is responsible for the effect produced, the experiment would produce stronger proof if the results were replicated in larger treatment and control groups.

Selecting groups entails assigning subjects in the groups of an experiment in such a way that treatment and control groups are comparable in all respects except the application of the treatment. Groups can be created in two ways: matching and randomization. In the MegaGro experiment discussed below, the plants might be matched according to characteristics such as age, weight and whether they are blooming. This involves distributing these plants so that each plant in one group exactly matches characteristics of plants in the other groups. Matching may be problematic, though, because it "can promote a false sense of security by leading [the experimenter] to believe that [the] experimental and control groups were really equated at the outset, when in fact they were not equated on a host of variables" (Jones, 291). In other words, you may have flowers for your MegaGro experiment that you matched and distributed among groups, but other variables are unaccounted for. It would be difficult to have equal groupings.

Randomization, then, is preferred to matching. This method is based on the statistical principle of normal distribution. Theoretically, any arbitrarily selected group of adequate size will reflect normal distribution. Differences between groups will average out and become more comparable. The principle of normal distribution states that in a population most individuals will fall within the middle range of values for a given characteristic, with increasingly fewer toward either extreme (graphically represented as the ubiquitous "bell curve").

Differences between Quasi-Experimental and Experimental Research

Thus far, we have explained that for experimental research we need:

a hypothesis for a causal relationship;
a control group and a treatment group;
to eliminate confounding variables that might mess up the experiment and prevent displaying the causal relationship; and
to have larger groups with a carefully sorted constituency; preferably randomized, in order to keep accidental differences from fouling things up.

But what if we don't have all of those? Do we still have an experiment? Not a true experiment in the strictest scientific sense of the term, but we can have a quasi-experiment, an attempt to uncover a causal relationship, even though the researcher cannot control all the factors that might affect the outcome.

A quasi-experimenter treats a given situation as an experiment even though it is not wholly by design. The independent variable may not be manipulated by the researcher, treatment and control groups may not be randomized or matched, or there may be no control group. The researcher is limited in what he or she can say conclusively.

The significant element of both experiments and quasi-experiments is the measure of the dependent variable, which it allows for comparison. Some data is quite straightforward, but other measures, such as level of self-confidence in writing ability, increase in creativity or in reading comprehension are inescapably subjective. In such cases, quasi-experimentation often involves a number of strategies to compare subjectivity, such as rating data, testing, surveying, and content analysis.

Rating essentially is developing a rating scale to evaluate data. In testing, experimenters and quasi-experimenters use ANOVA (Analysis of Variance) and ANCOVA (Analysis of Co-Variance) tests to measure differences between control and experimental groups, as well as different correlations between groups.

Since we're mentioning the subject of statistics, note that experimental or quasi-experimental research cannot state beyond a shadow of a doubt that a single cause will always produce any one effect. They can do no more than show a probability that one thing causes another. The probability that a result is the due to random chance is an important measure of statistical analysis and in experimental research.

Example: Causality

Let's say you want to determine that your new fertilizer, MegaGro, will increase the growth rate of plants. You begin by getting a plant to go with your fertilizer. Since the experiment is concerned with proving that MegaGro works, you need another plant, using no fertilizer at all on it, to compare how much change your fertilized plant displays. This is what is known as a control group.

Set up with a control group, which will receive no treatment, and an experimental group, which will get MegaGro, you must then address those variables that could invalidate your experiment. This can be an extensive and exhaustive process. You must ensure that you use the same plant; that both groups are put in the same kind of soil; that they receive equal amounts of water and sun; that they receive the same amount of exposure to carbon-dioxide-exhaling researchers, and so on. In short, any other variable that might affect the growth of those plants, other than the fertilizer, must be the same for both plants. Otherwise, you can't prove absolutely that MegaGro is the only explanation for the increased growth of one of those plants.

Such an experiment can be done on more than two groups. You may not only want to show that MegaGro is an effective fertilizer, but that it is better than its competitor brand of fertilizer, Plant! All you need to do, then, is have one experimental group receiving MegaGro, one receiving Plant! and the other (the control group) receiving no fertilizer. Those are the only variables that can be different between the three groups; all other variables must be the same for the experiment to be valid.

Controlling variables allows the researcher to identify conditions that may affect the experiment's outcome. This may lead to alternative explanations that the researcher is willing to entertain in order to isolate only variables judged significant. In the MegaGro experiment, you may be concerned with how fertile the soil is, but not with the plants'; relative position in the window, as you don't think that the amount of shade they get will affect their growth rate. But what if it did? You would have to go about eliminating variables in order to determine which is the key factor. What if one receives more shade than the other and the MegaGro plant, which received more shade, died? This might prompt you to formulate a plausible alternative explanation, which is a way of accounting for a result that differs from what you expected. You would then want to redo the study with equal amounts of sunlight.

Methods: Five Steps

Experimental research can be roughly divided into five phases:

Identifying a research problem

The process starts by clearly identifying the problem you want to study and considering what possible methods will affect a solution. Then you choose the method you want to test, and formulate a hypothesis to predict the outcome of the test.

For example, you may want to improve student essays, but you don't believe that teacher feedback is enough. You hypothesize that some possible methods for writing improvement include peer workshopping, or reading more example essays. Favoring the former, your experiment would try to determine if peer workshopping improves writing in high school seniors. You state your hypothesis: peer workshopping prior to turning in a final draft will improve the quality of the student's essay.

Planning an experimental research study

The next step is to devise an experiment to test your hypothesis. In doing so, you must consider several factors. For example, how generalizable do you want your end results to be? Do you want to generalize about the entire population of high school seniors everywhere, or just the particular population of seniors at your specific school? This will determine how simple or complex the experiment will be. The amount of time funding you have will also determine the size of your experiment.

Continuing the example from step one, you may want a small study at one school involving three teachers, each teaching two sections of the same course. The treatment in this experiment is peer workshopping. Each of the three teachers will assign the same essay assignment to both classes; the treatment group will participate in peer workshopping, while the control group will receive only teacher comments on their drafts.

Conducting the experiment

At the start of an experiment, the control and treatment groups must be selected. Whereas the "hard" sciences have the luxury of attempting to create truly equal groups, educators often find themselves forced to conduct their experiments based on self-selected groups, rather than on randomization. As was highlighted in the Basic Concepts section, this makes the study a quasi-experiment, since the researchers cannot control all of the variables.

For the peer workshopping experiment, let's say that it involves six classes and three teachers with a sample of students randomly selected from all the classes. Each teacher will have a class for a control group and a class for a treatment group. The essay assignment is given and the teachers are briefed not to change any of their teaching methods other than the use of peer workshopping. You may see here that this is an effort to control a possible variable: teaching style variance.

Analyzing the data

The fourth step is to collect and analyze the data. This is not solely a step where you collect the papers, read them, and say your methods were a success. You must show how successful. You must devise a scale by which you will evaluate the data you receive, therefore you must decide what indicators will be, and will not be, important.

Continuing our example, the teachers' grades are first recorded, then the essays are evaluated for a change in sentence complexity, syntactical and grammatical errors, and overall length. Any statistical analysis is done at this time if you choose to do any. Notice here that the researcher has made judgments on what signals improved writing. It is not simply a matter of improved teacher grades, but a matter of what the researcher believes constitutes improved use of the language.

Writing the paper/presentation describing the findings

Once you have completed the experiment, you will want to share findings by publishing academic paper (or presentations). These papers usually have the following format, but it is not necessary to follow it strictly. Sections can be combined or not included, depending on the structure of the experiment, and the journal to which you submit your paper.

Abstract : Summarize the project: its aims, participants, basic methodology, results, and a brief interpretation.
Introduction : Set the context of the experiment.
Review of Literature : Provide a review of the literature in the specific area of study to show what work has been done. Should lead directly to the author's purpose for the study.
Statement of Purpose : Present the problem to be studied.
Participants : Describe in detail participants involved in the study; e.g., how many, etc. Provide as much information as possible.
Materials and Procedures : Clearly describe materials and procedures. Provide enough information so that the experiment can be replicated, but not so much information that it becomes unreadable. Include how participants were chosen, the tasks assigned them, how they were conducted, how data were evaluated, etc.
Results : Present the data in an organized fashion. If it is quantifiable, it is analyzed through statistical means. Avoid interpretation at this time.
Discussion : After presenting the results, interpret what has happened in the experiment. Base the discussion only on the data collected and as objective an interpretation as possible. Hypothesizing is possible here.
Limitations : Discuss factors that affect the results. Here, you can speculate how much generalization, or more likely, transferability, is possible based on results. This section is important for quasi-experimentation, since a quasi-experiment cannot control all of the variables that might affect the outcome of a study. You would discuss what variables you could not control.
Conclusion : Synthesize all of the above sections.
References : Document works cited in the correct format for the field.

Experimental and Quasi-Experimental Research: Issues and Commentary

Several issues are addressed in this section, including the use of experimental and quasi-experimental research in educational settings, the relevance of the methods to English studies, and ethical concerns regarding the methods.

Using Experimental and Quasi-Experimental Research in Educational Settings

Charting causal relationships in human settings.

Any time a human population is involved, prediction of casual relationships becomes cloudy and, some say, impossible. Many reasons exist for this; for example,

researchers in classrooms add a disturbing presence, causing students to act abnormally, consciously or unconsciously;
subjects try to please the researcher, just because of an apparent interest in them (known as the Hawthorne Effect); or, perhaps
the teacher as researcher is restricted by bias and time pressures.

But such confounding variables don't stop researchers from trying to identify causal relationships in education. Educators naturally experiment anyway, comparing groups, assessing the attributes of each, and making predictions based on an evaluation of alternatives. They look to research to support their intuitive practices, experimenting whenever they try to decide which instruction method will best encourage student improvement.

Combining Theory, Research, and Practice

The goal of educational research lies in combining theory, research, and practice. Educational researchers attempt to establish models of teaching practice, learning styles, curriculum development, and countless other educational issues. The aim is to "try to improve our understanding of education and to strive to find ways to have understanding contribute to the improvement of practice," one writer asserts (Floden 1996, p. 197).

In quasi-experimentation, researchers try to develop models by involving teachers as researchers, employing observational research techniques. Although results of this kind of research are context-dependent and difficult to generalize, they can act as a starting point for further study. The "educational researcher . . . provides guidelines and interpretive material intended to liberate the teacher's intelligence so that whatever artistry in teaching the teacher can achieve will be employed" (Eisner 1992, p. 8).

Bias and Rigor

Critics contend that the educational researcher is inherently biased, sample selection is arbitrary, and replication is impossible. The key to combating such criticism has to do with rigor. Rigor is established through close, proper attention to randomizing groups, time spent on a study, and questioning techniques. This allows more effective application of standards of quantitative research to qualitative research.

Often, teachers cannot wait to for piles of experimentation data to be analyzed before using the teaching methods (Lauer and Asher 1988). They ultimately must assess whether the results of a study in a distant classroom are applicable in their own classrooms. And they must continuously test the effectiveness of their methods by using experimental and qualitative research simultaneously. In addition to statistics (quantitative), researchers may perform case studies or observational research (qualitative) in conjunction with, or prior to, experimentation.

Relevance to English Studies

Situations in english studies that might encourage use of experimental methods.

Whenever a researcher would like to see if a causal relationship exists between groups, experimental and quasi-experimental research can be a viable research tool. Researchers in English Studies might use experimentation when they believe a relationship exists between two variables, and they want to show that these two variables have a significant correlation (or causal relationship).

A benefit of experimentation is the ability to control variables, such as the amount of treatment, when it is given, to whom and so forth. Controlling variables allows researchers to gain insight into the relationships they believe exist. For example, a researcher has an idea that writing under pseudonyms encourages student participation in newsgroups. Researchers can control which students write under pseudonyms and which do not, then measure the outcomes. Researchers can then analyze results and determine if this particular variable alone causes increased participation.

Transferability-Applying Results

Experimentation and quasi-experimentation allow for generating transferable results and accepting those results as being dependent upon experimental rigor. It is an effective alternative to generalizability, which is difficult to rely upon in educational research. English scholars, reading results of experiments with a critical eye, ultimately decide if results will be implemented and how. They may even extend that existing research by replicating experiments in the interest of generating new results and benefiting from multiple perspectives. These results will strengthen the study or discredit findings.

Concerns English Scholars Express about Experiments

Researchers should carefully consider if a particular method is feasible in humanities studies, and whether it will yield the desired information. Some researchers recommend addressing pertinent issues combining several research methods, such as survey, interview, ethnography, case study, content analysis, and experimentation (Lauer and Asher, 1988).

Advantages and Disadvantages of Experimental Research: Discussion

In educational research, experimentation is a way to gain insight into methods of instruction. Although teaching is context specific, results can provide a starting point for further study. Often, a teacher/researcher will have a "gut" feeling about an issue which can be explored through experimentation and looking at causal relationships. Through research intuition can shape practice .

A preconception exists that information obtained through scientific method is free of human inconsistencies. But, since scientific method is a matter of human construction, it is subject to human error . The researcher's personal bias may intrude upon the experiment , as well. For example, certain preconceptions may dictate the course of the research and affect the behavior of the subjects. The issue may be compounded when, although many researchers are aware of the affect that their personal bias exerts on their own research, they are pressured to produce research that is accepted in their field of study as "legitimate" experimental research.

The researcher does bring bias to experimentation, but bias does not limit an ability to be reflective . An ethical researcher thinks critically about results and reports those results after careful reflection. Concerns over bias can be leveled against any research method.

Often, the sample may not be representative of a population, because the researcher does not have an opportunity to ensure a representative sample. For example, subjects could be limited to one location, limited in number, studied under constrained conditions and for too short a time.

Despite such inconsistencies in educational research, the researcher has control over the variables , increasing the possibility of more precisely determining individual effects of each variable. Also, determining interaction between variables is more possible.

Even so, artificial results may result . It can be argued that variables are manipulated so the experiment measures what researchers want to examine; therefore, the results are merely contrived products and have no bearing in material reality. Artificial results are difficult to apply in practical situations, making generalizing from the results of a controlled study questionable. Experimental research essentially first decontextualizes a single question from a "real world" scenario, studies it under controlled conditions, and then tries to recontextualize the results back on the "real world" scenario. Results may be difficult to replicate .

Perhaps, groups in an experiment may not be comparable . Quasi-experimentation in educational research is widespread because not only are many researchers also teachers, but many subjects are also students. With the classroom as laboratory, it is difficult to implement randomizing or matching strategies. Often, students self-select into certain sections of a course on the basis of their own agendas and scheduling needs. Thus when, as often happens, one class is treated and the other used for a control, the groups may not actually be comparable. As one might imagine, people who register for a class which meets three times a week at eleven o'clock in the morning (young, no full-time job, night people) differ significantly from those who register for one on Monday evenings from seven to ten p.m. (older, full-time job, possibly more highly motivated). Each situation presents different variables and your group might be completely different from that in the study. Long-term studies are expensive and hard to reproduce. And although often the same hypotheses are tested by different researchers, various factors complicate attempts to compare or synthesize them. It is nearly impossible to be as rigorous as the natural sciences model dictates.

Even when randomization of students is possible, problems arise. First, depending on the class size and the number of classes, the sample may be too small for the extraneous variables to cancel out. Second, the study population is not strictly a sample, because the population of students registered for a given class at a particular university is obviously not representative of the population of all students at large. For example, students at a suburban private liberal-arts college are typically young, white, and upper-middle class. In contrast, students at an urban community college tend to be older, poorer, and members of a racial minority. The differences can be construed as confounding variables: the first group may have fewer demands on its time, have less self-discipline, and benefit from superior secondary education. The second may have more demands, including a job and/or children, have more self-discipline, but an inferior secondary education. Selecting a population of subjects which is representative of the average of all post-secondary students is also a flawed solution, because the outcome of a treatment involving this group is not necessarily transferable to either the students at a community college or the students at the private college, nor are they universally generalizable.

When a human population is involved, experimental research becomes concerned if behavior can be predicted or studied with validity. Human response can be difficult to measure . Human behavior is dependent on individual responses. Rationalizing behavior through experimentation does not account for the process of thought, making outcomes of that process fallible (Eisenberg, 1996).

Nevertheless, we perform experiments daily anyway . When we brush our teeth every morning, we are experimenting to see if this behavior will result in fewer cavities. We are relying on previous experimentation and we are transferring the experimentation to our daily lives.

Moreover, experimentation can be combined with other research methods to ensure rigor . Other qualitative methods such as case study, ethnography, observational research and interviews can function as preconditions for experimentation or conducted simultaneously to add validity to a study.

We have few alternatives to experimentation. Mere anecdotal research , for example is unscientific, unreplicatable, and easily manipulated. Should we rely on Ed walking into a faculty meeting and telling the story of Sally? Sally screamed, "I love writing!" ten times before she wrote her essay and produced a quality paper. Therefore, all the other faculty members should hear this anecdote and know that all other students should employ this similar technique.

On final disadvantage: frequently, political pressure drives experimentation and forces unreliable results. Specific funding and support may drive the outcomes of experimentation and cause the results to be skewed. The reader of these results may not be aware of these biases and should approach experimentation with a critical eye.

Advantages and Disadvantages of Experimental Research: Quick Reference List

Experimental and quasi-experimental research can be summarized in terms of their advantages and disadvantages. This section combines and elaborates upon many points mentioned previously in this guide.


gain insight into methods of instruction	subject to human error
intuitive practice shaped by research	personal bias of researcher may intrude
teachers have bias but can be reflective	sample may not be representative
researcher can have control over variables	can produce artificial results
humans perform experiments anyway	results may only apply to one situation and may be difficult to replicate
can be combined with other research methods for rigor	groups may not be comparable
use to determine what is best for population	human response can be difficult to measure
provides for greater transferability than anecdotal research	political pressure may skew results

Ethical Concerns

Experimental research may be manipulated on both ends of the spectrum: by researcher and by reader. Researchers who report on experimental research, faced with naive readers of experimental research, encounter ethical concerns. While they are creating an experiment, certain objectives and intended uses of the results might drive and skew it. Looking for specific results, they may ask questions and look at data that support only desired conclusions. Conflicting research findings are ignored as a result. Similarly, researchers, seeking support for a particular plan, look only at findings which support that goal, dismissing conflicting research.

Editors and journals do not publish only trouble-free material. As readers of experiments members of the press might report selected and isolated parts of a study to the public, essentially transferring that data to the general population which may not have been intended by the researcher. Take, for example, oat bran. A few years ago, the press reported how oat bran reduces high blood pressure by reducing cholesterol. But that bit of information was taken out of context. The actual study found that when people ate more oat bran, they reduced their intake of saturated fats high in cholesterol. People started eating oat bran muffins by the ton, assuming a causal relationship when in actuality a number of confounding variables might influence the causal link.

Ultimately, ethical use and reportage of experimentation should be addressed by researchers, reporters and readers alike.

Reporters of experimental research often seek to recognize their audience's level of knowledge and try not to mislead readers. And readers must rely on the author's skill and integrity to point out errors and limitations. The relationship between researcher and reader may not sound like a problem, but after spending months or years on a project to produce no significant results, it may be tempting to manipulate the data to show significant results in order to jockey for grants and tenure.

Meanwhile, the reader may uncritically accept results that receive validity by being published in a journal. However, research that lacks credibility often is not published; consequentially, researchers who fail to publish run the risk of being denied grants, promotions, jobs, and tenure. While few researchers are anything but earnest in their attempts to conduct well-designed experiments and present the results in good faith, rhetorical considerations often dictate a certain minimization of methodological flaws.

Concerns arise if researchers do not report all, or otherwise alter, results. This phenomenon is counterbalanced, however, in that professionals are also rewarded for publishing critiques of others' work. Because the author of an experimental study is in essence making an argument for the existence of a causal relationship, he or she must be concerned not only with its integrity, but also with its presentation. Achieving persuasiveness in any kind of writing involves several elements: choosing a topic of interest, providing convincing evidence for one's argument, using tone and voice to project credibility, and organizing the material in a way that meets expectations for a logical sequence. Of course, what is regarded as pertinent, accepted as evidence, required for credibility, and understood as logical varies according to context. If the experimental researcher hopes to make an impact on the community of professionals in their field, she must attend to the standards and orthodoxy's of that audience.

Annotated Bibliography

A cozy world of trivial pursuits? (1996, June 28) The Times Educational Supplement . 4174, pp. 14-15.

A critique discounting the current methods Great Britain employs to fund and disseminate educational research. The belief is that research is performed for fellow researchers not the teaching public and implications for day to day practice are never addressed.

Anderson, J. A. (1979, Nov. 10-13). Research as argument: the experimental form. Paper presented at the annual meeting of the Speech Communication Association, San Antonio, TX.

In this paper, the scientist who uses the experimental form does so in order to explain that which is verified through prediction.

Anderson, Linda M. (1979). Classroom-based experimental studies of teaching effectiveness in elementary schools . (Technical Report UTR&D-R- 4102). Austin: Research and Development Center for Teacher Education, University of Texas.

Three recent large-scale experimental studies have built on a database established through several correlational studies of teaching effectiveness in elementary school.

Asher, J. W. (1976). Educational research and evaluation methods . Boston: Little, Brown.

Abstract unavailable by press time.

Babbie, Earl R. (1979). The Practice of Social Research . Belmont, CA: Wadsworth.

A textbook containing discussions of several research methodologies used in social science research.

Bangert-Drowns, R.L. (1993). The word processor as instructional tool: a meta-analysis of word processing in writing instruction. Review of Educational Research, 63 (1), 69-93.

Beach, R. (1993). The effects of between-draft teacher evaluation versus student self-evaluation on high school students' revising of rough drafts. Research in the Teaching of English, 13 , 111-119.

The question of whether teacher evaluation or guided self-evaluation of rough drafts results in increased revision was addressed in Beach's study. Differences in the effects of teacher evaluations, guided self-evaluation (using prepared guidelines,) and no evaluation of rough drafts were examined. The final drafts of students (10th, 11th, and 12th graders) were compared with their rough drafts and rated by judges according to degree of change.

Beishuizen, J. & Moonen, J. (1992). Research in technology enriched schools: a case for cooperation between teachers and researchers . (ERIC Technical Report ED351006).

This paper describes the research strategies employed in the Dutch Technology Enriched Schools project to encourage extensive and intensive use of computers in a small number of secondary schools, and to study the effects of computer use on the classroom, the curriculum, and school administration and management.

Borg, W. P. (1989). Educational Research: an Introduction . (5th ed.). New York: Longman.

An overview of educational research methodology, including literature review and discussion of approaches to research, experimental design, statistical analysis, ethics, and rhetorical presentation of research findings.

Campbell, D. T., & Stanley, J. C. (1963). Experimental and quasi-experimental designs for research . Boston: Houghton Mifflin.

A classic overview of research designs.

Campbell, D.T. (1988). Methodology and epistemology for social science: selected papers . ed. E. S. Overman. Chicago: University of Chicago Press.

This is an overview of Campbell's 40-year career and his work. It covers in seven parts measurement, experimental design, applied social experimentation, interpretive social science, epistemology and sociology of science. Includes an extensive bibliography.

Caporaso, J. A., & Roos, Jr., L. L. (Eds.). Quasi-experimental approaches: Testing theory and evaluating policy. Evanston, WA: Northwestern University Press.

A collection of articles concerned with explicating the underlying assumptions of quasi-experimentation and relating these to true experimentation. With an emphasis on design. Includes a glossary of terms.

Collier, R. Writing and the word processor: How wary of the gift-giver should we be? Unpublished manuscript.

Unpublished typescript. Charts the developments to date in computers and composition and speculates about the future within the framework of Willie Sypher's model of the evolution of creative discovery.

Cook, T.D. & Campbell, D.T. (1979). Quasi-experimentation: design and analysis issues for field settings . Boston: Houghton Mifflin Co.

The authors write that this book "presents some quasi-experimental designs and design features that can be used in many social research settings. The designs serve to probe causal hypotheses about a wide variety of substantive issues in both basic and applied research."

Cutler, A. (1970). An experimental method for semantic field study. Linguistic Communication, 2 , N. pag.

This paper emphasizes the need for empirical research and objective discovery procedures in semantics, and illustrates a method by which these goals may be obtained.

Daniels, L. B. (1996, Summer). Eisenberg's Heisenberg: The indeterminancies of rationality. Curriculum Inquiry, 26 , 181-92.

Places Eisenberg's theories in relation to the death of foundationalism by showing that he distorts rational studies into a form of relativism. He looks at Eisenberg's ideas on indeterminacy, methods and evidence, what he is against and what we should think of what he says.

Danziger, K. (1990). Constructing the subject: Historical origins of psychological research. Cambridge: Cambridge University Press.

Danzinger stresses the importance of being aware of the framework in which research operates and of the essentially social nature of scientific activity.

Diener, E., et al. (1972, December). Leakage of experimental information to potential future subjects by debriefed subjects. Journal of Experimental Research in Personality , 264-67.

Research regarding research: an investigation of the effects on the outcome of an experiment in which information about the experiment had been leaked to subjects. The study concludes that such leakage is not a significant problem.

Dudley-Marling, C., & Rhodes, L. K. (1989). Reflecting on a close encounter with experimental research. Canadian Journal of English Language Arts. 12 , 24-28.

Researchers, Dudley-Marling and Rhodes, address some problems they met in their experimental approach to a study of reading comprehension. This article discusses the limitations of experimental research, and presents an alternative to experimental or quantitative research.

Edgington, E. S. (1985). Random assignment and experimental research. Educational Administration Quarterly, 21 , N. pag.

Edgington explores ways on which random assignment can be a part of field studies. The author discusses both non-experimental and experimental research and the need for using random assignment.

Eisenberg, J. (1996, Summer). Response to critiques by R. Floden, J. Zeuli, and L. Daniels. Curriculum Inquiry, 26 , 199-201.

A response to critiques of his argument that rational educational research methods are at best suspect and at worst futile. He believes indeterminacy controls this method and worries that chaotic research is failing students.

Eisner, E. (1992, July). Are all causal claims positivistic? A reply to Francis Schrag. Educational Researcher, 21 (5), 8-9.

Eisner responds to Schrag who claimed that critics like Eisner cannot escape a positivistic paradigm whatever attempts they make to do so. Eisner argues that Schrag essentially misses the point for trying to argue for the paradigm solely on the basis of cause and effect without including the rest of positivistic philosophy. This weakens his argument against multiple modal methods, which Eisner argues provides opportunities to apply the appropriate research design where it is most applicable.

Floden, R.E. (1996, Summer). Educational research: limited, but worthwhile and maybe a bargain. (response to J.A. Eisenberg). Curriculum Inquiry, 26 , 193-7.

Responds to John Eisenberg critique of educational research by asserting the connection between improvement of practice and research results. He places high value of teacher discrepancy and knowledge that research informs practice.

Fortune, J. C., & Hutson, B. A. (1994, March/April). Selecting models for measuring change when true experimental conditions do not exist. Journal of Educational Research, 197-206.

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Citation Information

Luann Barnes, Jennifer Hauser, Luana Heikes, Anthony J. Hernandez, Paul Tim Richard, Katherine Ross, Guo Hua Yang, and Mike Palmquist. (1994-2024). Experimental and Quasi-Experimental Research. The WAC Clearinghouse. Colorado State University. Available at https://wac.colostate.edu/repository/writing/guides/.

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Published: 25 August 2024

Comparison of the SBAR method and modified handover model on handover quality and nurse perception in the emergency department: a quasi-experimental study

Atefeh Alizadeh-risani 1 ,
Fatemeh Mohammadkhah 2 ,
Ali Pourhabib 2 ,
Zahra Fotokian 2 , 4 &
Marziyeh Khatooni 3

BMC Nursing volume 23 , Article number: 585 ( 2024 ) Cite this article

Metrics details

Effective information transfer during nursing shift handover is a crucial component of safe care in the emergency department (ED). Examining nursing handover models shows that they are frequently associated with errors. Disadvantages of the SBAR handover model include uncertainty of nursing staff regarding transfer of responsibility and non-confidentiality of patient information. To increase reliability of handover, written forms and templates can be used in addition to oral handover by the bedside.

The purpose of this study is to compare the ‘Situation, Background, Assessment, Recommendation (SBAR) method and modified handover model on the handover quality and nurse perception of shift handover in the ED.

This research was designed as a semi-experimental study, with census survey method used for sampling. In order to collect data, Nurse Perception of Hanover Questionnaire (NPHQ) and Handover Quality Rating Tool (HQRT) were used after translating and confirming validity and reliability used to direct/collect data. A total of 31 nurses working in the ED received training on the modified shift handover model in a one-hour theory session and three hands-on bedside training sessions. This model was implemented by the nurses for one month. Data was analyzed with SPSS (version 26) using paired t-tests and analysis of covariance.

Results indicated significant difference between the modified handover model and SBAR in components of information transfer ( P < 0.001), shared understanding ( P < 0.001), working atmosphere ( P = 0.004), handover quality ( P < 0.001), and nurse perception of handover ( P < 0.001). The univariate covariance test did not show demographic variables to be significantly correlated with handover perception or handover quality in SBAR and modified methods ( P > 0.05).

Conclusions

The results of this study can be presented to nursing managers as a guide in improving the quality of nursing care via implementing and applying the modified handover model in the nursing handover. The resistance of nurses against executing a new handover method was one of the limitations of the research, which was resolved by explanation of the plan and goals, as well as the cooperation of the hospital matron, and the ward supervisor. It is suggested to carry out a similar investigation in other hospital departments and contrast the outcomes with those obtained in the current study.

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Introduction

One of the professional responsibilities of nurses in delivering high-quality and safe nursing care is the handover process [ 1 ]. This concept refers to the process of transferring the responsibility of care and patient information from one caregiver to another, in order to continue the care of the patient [ 2 ]. Effective information transfer during nursing shift handover is considered a vital component of safe care in the Emergency Department (ED). Some challenges in providing accurate information during handover include providing excessive or insufficient information, lack of a checklist, and delays in handover [ 3 ]. Incomplete transmission of information increases the occurrence of errors, leads to inappropriate treatment, delays diagnosis and treatment, and increases physician and nursing errors and treatment costs [ 4 ]. A study by Spooner showed that 80% of serious medical care errors are related to nursing handovers, and one fifth of patients suffer from complications due to handover errors [ 5 ]. A review of 3000 sentinel events demonstrated that a communication breakdown occurred 65–70% of the time. It has been demonstrated that poor communication handovers result in adverse events, delays in treatment, redundancies that impact efficiencies and effectiveness, low patient and healthcare provider satisfaction, and more admissions [ 3 ].

There are various nursing handover methods, including oral handover, and the use of special forms [ 6 ]. The oral handover method at the bedside can lead to better communication, improved patient care, and increased patient satisfaction [ 7 ]. So far, several shift handover tools have been developed in hospital departments, including: ISOBAR [ 8 ], ISBAR [ 9 ], SBAR [ 3 ], REED [ 10 ], ICCCO [ 11 ], VITAL and PVITAL [ 12 ] and the modified nursing handover model [ 13 ]. Examining nursing handover models shows that they are frequently associated with errors [ 14 ]. While a format to use for a handover was the topic of study in several of the nursing studies [ 15 , 16 , 17 , 18 ], accuracy of content and outcomes were not included. Barriers and facilitators to nursing handovers were identified, but evidence for best practice was not evident. Various strategies have been developed to enhance the effectiveness and efficiency of nursing handover, including standardized approaches, bedside handover and technology. The majority of these models have been evaluated in inpatient settings; few have been conducted in the ED. Among these shift handover models, the PVITAL model was specifically designed for the ED and includes components of Present patient, Intake and output, Treatment and diagnosis, Admission and discharge, and Legal and documentation. Despite the positive aspects, this model has inconsistencies that question its effectiveness in nursing shift handovers [ 13 ]. Also, one of the most widely used shift handover is the SBAR model [ 19 ]. The SBAR model includes Situation, Background, Assessment, and Recommendation components. SBAR is an information tool that transmits standardized information and makes reports concise, targeted and relevant, and facilitates information exchanges, and can be improved by involving the patient in delivery and transformation [ 20 ]. The SBAR handover model was proposed by the joint commission with the aim of reducing errors and increasing the quality of care. This model was initially designed by Leonard and Graham for use in health care systems [ 3 ]. In 2013, adoption of this model for nursing handovers was announced mandatory by the Deputy Minister of Nursing of Iran Ministry of Health [ 21 ]. Currently, this model is only implemented orally at the patient bedside [ 22 ]. Disadvantages of this model include uncertainty of nursing staff regarding transfer of responsibility and non-confidentiality of patient information. To increase reliability of handover, written forms and templates can be used in addition to oral and face-to-face handover by the bedside [ 23 ]. In this regard, the modified nursing handover model was first designed by Klim et al. (2013) for shift handover in the ED. This method has a written form and template and includes components of identification and alert, assessment and progress, nursing care need, plan, and alerting the nurse in charge/medical officer based on vital sign parameters or clinical deterioration [ 24 ]. Findings of a study by Kerr (2016) showed that implementation of this model improves transmission of important information to nurses in subsequent shifts, leading to an increase in participation of patients and their companions in the handover process [ 13 ].

The use of a simple, structured, and standard model with a written template in nursing handovers is one of the elements influencing provision of appropriate services. According to research, implementation of the modified handover model in Iran has not been investigated to date. Despite the widespread use of SBAR, there is limited comparative research on its effectiveness relative to modified handover models in emergency settings. We hypothesize that the modified model will result in fewer handover errors compared to the SBAR method. This study aims to compare the effectiveness of the SBAR method and modified handover model on handover quality and nurse perception in the ED.

Materials and methods

This research was designed as a pre-post intervention, semi-experimental study, with census survey method used for sampling.

Participants

The study location was the ED of Zakaria Razi Social Security Hospital in Qazvin, Iran. The sample size was selected through a census of nurses working in the ED of Zakariya Razi Hospital in Qazvin. There were 45 nurses working in the emergency department, including 38 nurses, one head nurse, one assistant head nurse (staff), three triage nurses and two outpatient operating room nurses. Six nurses had less than six months of work experience in the ED and were not included in the study according to the inclusion criteria. Considering a Cohen’s effect size of 0.52 (based on a pilot sample of the dependent variable, quality of shift handover), with a Type I error rate of 5% and a statistical power of test 80%, the sample size was estimated to be 32 individuals using GPOWER software. A total of 32 nurses were included in the study, but one nurse withdrew from participation, resulting in a final sample size of 31 nurses. The inclusion criteria comprised willingness to participate in the study, and at least 6 months of working experience in the ED. Unwillingness to continue cooperation was set as one of the exclusion criteria.

Data collection (procedures)

Initially, the researcher made a list of the nurses employed in the ED. The nurses were then introduced to the study and its objectives, and participants were selected based on inclusion criteria and obtaining informed consent to participate in the study. The SBAR model was routinely implemented orally in the ED. At the beginning of the research, Nurse Perception of Hanover Questionnaire (NPHQ) and Handover Quality Rating Tool (HQRT) were completed by all participants. Owing to lack of familiarity with the modified handover model, nurses were educated via a one-hour theory session in the hospital conference hall, where the items of the modified nursing handover checklist and how to complete it were taught using PowerPoint and a whiteboard. Three hands-on training sessions was individually held for all nurses explaining the handover model, how to fill out the checklist and use the checklist during shift handover at the patient’s bedside. In order to resolve ambiguities and questions, we communicated with the participants through cyberspace. Brainstorming, clear explanations, effective communication, and receiving feedback were used for more productive training sessions. Moreover, the modified handover checklist was designed by the researcher and provided to the nurses for better understanding of the contents. Subsequently, the modified handover model was implemented by the participants for one month [ 13 ]. During this month, about 350 shift handovers were made with the modified handover method. In order to ensure proper implementation, the researcher attended and directly supervised all handover situations involving the target group. After implementation of the modified handover model, NPHQ and HQRT were completed once more by the participants (Fig. 1 ).

The process of implementing the modified nursing handover model

Data collection

Instruments

Demographic information : included variables of age, gender, marital status, level of education, employment type, years of work experience, years of work experience in the ED, working conditions in terms of shifts.

Nurse handover perception questionnaire (NHPQ) : This 22-item questionnaire reveals perception and performance of nurses regarding shift handover. The first half of the NHPQ examines perceptions regarding current practices and essential components of handover [ 15 ]. The second half of the NHPQ, reviews nurse views regarding bedside handover [ 23 ]. The items in the NHPQ questionnaire include a series of statements about nurses’ general understanding of shift handover and their experiences of clinical shift handover at the bedside. This tool is scored on a 4-point Likert scale, with scores ranging from 22 to 88. A higher score indicates a higher perception of handover. Eight items of this questionnaire [ 3 , 4 , 8 , 10 , 17 , 20 , 21 ] are scored negatively. Content validity was reported using a content validity index (CVI) of 0.92, which indicated satisfactory content validity. The internal reliability of the questionnaire items was determined using Cronbach’s alpha of 0.99. The one-dimensional Intraclass Correlation Coefficient (ICC) for the internal homogeneity test of the items was 0.92 [ 23 ].

Handover quality rating tool (HQRT) : The handover quality rating tool has been developed to evaluate the shift handover quality. This 16-item questionnaire includes five components of information transfer (items 1 to 7), shared understanding (items 8 to 10), working atmosphere (items 11 to 13), handover quality (item 14), and circumstances of the handover (items 15 and 16). This questionnaire is scored on a 4-point Likert scale, with the scores ranging from 16 to 64. A higher score indicates better handover quality [ 24 ]. A study reported the validity of this tool with a reliability coefficient of 0.67 [ 25 ].

The above questionnaires have not been used in Iran to date. Therefore, they were translated and validated in the present study, as part of a master’s thesis in internal-surgical nursing [ 26 ]. The results related to the process of translating the questionnaires are summarized as follows:

Getting permission from the tool designer;

Translation from the reference language (English) to the target language (Persian): In this study, two translators familiar with English performed the translation from the original language to Persian. The translation process was carried out independently by the two translators.

Consolidation and comparison of translations: At this stage, the researchers held a meeting to review the translated questionnaires in order to identify and eliminate inappropriate phrases or concepts in the translation. The original version and the translated versions were checked for any discrepancies. The translated versions were combined and a single version was developed.

Translation of the final translated version from the target language (Persian) to the original language (English): This translation was performed by two experts fluent in English. The translated versions were reviewed by the research team and discussed until a consensus was reached. Subsequently, the Persian questionnaires were distributed to ten faculty members to assess content validity, and to twenty nurses working in the ED to evaluate reliability. This process was conducted twice, with a gap of 10 days between each administration. After making necessary corrections, the final version of the questionnaire was prepared. In the present study, all items of the NHPQ and HQRT had a CVI above 0.88, which is acceptable. SCVI/UA was 0.86 and 0.87 for NHPQ and HQRT respectively. SCVI/AVE of both questionnaires was 0.98, which is in the acceptable range. CVR of all items of both questionnaires was above 0.62. Cronbach’s alpha coefficient was 0.93 for NHPQ and 0.96 for HQRT. Hence, the reliability of the tools was confirm [ 26 ].

Data analysis

Descriptive and inferential statistics were used for data analysis using SPSS software (version 24). Paired t-tests, chi-square and analysis of variance were used to compare the effect of SBAR and the modified handover models. P Value of < 0.05 was considered significant.

Nurse characteristics

The average age of the participants was 33 ± 4 years. Seventeen (54.8%) were women, and 22 (71%) were married. Thirty (96.8%) had a bachelor’s degree, and 23 (74.2%) were officially employed. Fourteen (45.2%) had a work experience of 6–10 years, while 16 (51.6%) had less than 5 years of work experience (Table 1 ).

According to paired t-test results, significant difference existed between the average handover quality of the SBAR model and the modified handover model ( P < 0.001). Accordingly, the average quality of handover in the modified handover model (57.64) was 8.09 units higher than the SBAR model (49.54). Also, based on paired t-test results, there was significant difference between the two models in components of information transfer ( P < 0.001), shared understanding ( P < 0.001), working atmosphere ( P = 0.004), and handover quality ( P < 0.001). Meanwhile, the component of circumstances of the handover, was not significantly different between the two models ( P = 0.227). Therefore, our findings indicated that handover quality and its components (except circumstances of the handover) were higher in the modified handover model compared with the SBAR model. Findings from the analysis of Cohen’s d effect size indicated that the modified handover model has a significantly greater influence on the quality of handover, being 1.29 times higher than the SBAR model. According to results, the modified handover model had the largest effect on the information transfer component with an effect size of 1.56 units, and the smallest effect on the circumstances of the handover with an effect size of 0.23 units (Table 2 ).

Results of the paired t-test revealed significant difference between the average nurse perception of handover in two models of SBAR and modified handover ( P < 0.001). The average nurse perception of handover was 9.64 units higher in the modified handover model (80.45) compared with the SBAR model (70.80). The results of Cohen’s d effect size showed that the modified handover model is 1.51 times more effective than the SBAR model on nurses’ perception of handover (Table 2 ).

The results of the paired t-test demonstrated that all items except “not enough time allowed”, “there was a tension between the team”, “the person handing over under pressure”, and “the person receiving under pressure”, were significantly different between the two models ( P < 0.05). Hence, comparing the two models according to Cohen’s effect size, the largest and smallest effect sizes belonged to the items “use of available documentation (charts, etc.)” (1.39) and “the person receiving under pressure” (0.16), respectively (Table 3 ).

Most of the information I receive during shift handover is not related to the patient under my care.

Noise interferes with my ability to concentrate during shift handover.

I believe effective communication skills (such as clear and calm speech) should be used in handover.

In my experience, shift handover is often disrupted by patients, companions or other staff.

After handover, I seek additional information about patients from another nurse or the nurse in charge.

I believe this shift handover model is time consuming.

According to calculated Cohen’s effect sizes, the largest and smallest effect sizes of the modified handover model in comparison with the SBAR method belonged to “I receive sufficient information on nursing care (activity, nutrition, hydration, and pain) during the shift handover” (1.54) and “I believe this shift handover model is time consuming” (0.024), respectively (Table 4 ).

Univariate covariance analysis was used to determine the relationship of demographic variables with nurse perception of handover and the quality of handover. Due to a quantitative nature, the age variable was entered as a covariate and other variables as factors. The results revealed that demographic variables do not have a significant effect on nurses’ perception of handover or the quality of handover in either of the two models ( P > 0.05).

The present study was conducted with the aim of comparing the effect of implementing SBAR and modified handover models on handover quality and nurse perception of handover in the ED. Based on our findings, implementation of the modified handover model has a more favorable effect on the average handover quality and nurse perception scores compared with the SBAR method. The modified handover model was first designed by Klim et al. (2013), by modifying the components of the SBAR model via group interviews in the ED (17). The modified handover model focused on a standardized approach, including checklists, with emphasis on nursing care and patient involvement. This handover model in the ED enhanced continuity of nursing care, and aspects of the way in which care was implemented and documented, which might translate to reduced incidence of adverse events in this setting. Improvements observed in this current study, such as application of charts for medication, vital signs, allergies, and fluid balance to review patient nursing care, and receiving sufficient information on nursing care (activity, nutrition, hydration, and pain) during the shift handover might help prevent adverse events, including medication errors and promoted handover quality.

Another component of the new handover model was that handover should be conducted in the cubicle at the bedside and involve the patient and/or their companion. More recently, it has been shown that family members also value the opportunity to participate in handover, which promotes family-centered care. Hence, there are disparate opinions between nurses, patients and their family about whether patients should participate in handover. Florin et al. suggest that nurses should establish patient preferences for the degree of their participation in care [ 27 ]. In a phenomenological study, Frank et al. found that ED patients want to be acknowledged; however, they struggle to become involved in their care. In this current study, handover was more likely to be conducted in front of the patient, and more patients had the opportunity to contribute to and/or listen to handover discussion after the introduction of the ED structured nursing handover framework [ 28 ].

Preliminary data showed that there was mixed opinion regarding the appropriate environment for inter-shift handover in the ED. The framework was specifically modified to address deficits in nursing care practice, effect on handover quality and nurse perception of handover. For example, emphasis was placed on viewing the patient’s charts for medication, vital signs and fluid balance. This provides an opportunity for omissions of information, documentation, or care to be identified and addressed at the commencement of a shift. The results of a study by Kerr (2016) demonstrated that implementation of this model improves the transfer of important information to nurses of subsequent shifts and does not possess the shortcomings of the SBAR model [ 13 ].

Accordingly, implementing the modified handover model, improves bedside handover quality from 62.5 to 93%, patient participation in the handover process from 42.1 to 80%, information transfer from 26.9 to 67.8%, identification of patients with allergies from 51.2 to 82%, the amount of documentation from 82.6 to 94.1%, and the use of charts and documentation during handover from 38.7 to 60.8%, meanwhile decreasing omission of essential information such as vital signs from 50 to 32.2%. The authors concluded that implementation of the modified handover model increases documentation, improves nursing care, improves receiving information, enhances patient participation during handover, reduces errors in care and documentation, and promotes bedside handover. A good quality handover facilitates the transfer of information, mutual understanding, and a good working environment [ 13 ]. These findings are consistent with the results of current study.

Moreover, Beigmoradi (2019) showed that in the SBAR model, less attention is paid to clinical records and evaluation of patient body systems during the handover [ 29 ].

Patients are treated urgently in the ED, with the goal of a comprehensive handover immediately. Meanwhile, the non-comprehensive handover model causes a halt in the flow of information, which reduces the handover efficiency. In contrast, the results of a study by Li et al. (2022) demonstrated that implementing a combined model of SBAR and mental map, leads to a significant improvement in the quality of handover and nurse perception of the patient, while reducing defects in shift handover [ 30 ]. Kazemi et al. (2016) showed that patient participation in the handover process increases patient and nurse satisfaction and helps inform patients of their care plan [ 22 ].

According to our findings, demographic variables do not have a significant effect on nurses’ perception of handover and the quality of handover in SBAR or modified handover models. The results of this study can be compared with the results of others in some aspects. Mamallalala et al. (2017) showed that there is significant difference between experience and information transfer of information during shift handover. Hence, nurses with an experience of more than 10 years show higher levels of shared communication and information transfer during shift handover [ 31 ]. The findings of the study by Zakrison et al. (2016) also demonstrated that more experienced nurses are more concerned about transferring information compared with the less experienced [ 32 ], which is not consistent with the results of the present study. The reason for this discrepancy may be the different characteristics of the study samples in the two studies.

The findings of the present study demonstrated that the modified handover model demonstrably improves Shift handover quality, Information transfer, Shared understanding and Perception of handover in the ED. Hence, the results of this study can be presented to nursing managers and quality improvement managers of hospitals as a guide in improving the quality of nursing care via implementing and applying this strategy in the nursing handover. The ED structured nursing modified handover framework focused on a standardized approach, including checklists, with emphasis on nursing care and patient involvement. This straightforward and easy-to-implement strategy has the potential to enhance continuity of care and completion of aspects of nursing care tasks and documentation in the ED.

Strengths and limitations

The present research is the first study to investigate the effect of the modified handover model on handover quality and nurses’ perception of handover in Iran.

The modified handover model tool is a reliable and validated tool that can be easily implemented in ED practice for sharing information among health care providers; however, there are limitations of use in patients with complex medical histories and care plans, especially in the critical care setting. In addition, the modified handover model tool requires training all clinical staff so that they can understand communication well. Future research might test whether introduction of this handover model in the ED setting results in actual enhanced patient safety, including reduction in medication errors.

The resistance of nurses against executing a new handover method was one of the limitations of the research, which was resolved by explanation of the plan and goals, as well as the cooperation of the hospital matron, and the ward supervisor.

Key points for policy, practice and/or research

The results of this study can provide nursing managers with a model of nursing shift handover that promotes the quality of nursing care and patient-related concepts. Interventions could target a combination of the content, communication method, and location aspects of the modified handover model.

Implementing a standardized handover framework such as the modified handover model method allows for concise and comprehensive information handoffs.

The modified handover model tool might be an adaptive tool that is suitable for many healthcare settings, in particular when clear and effective interpersonal communication is required.

The modified handover model provides an opportunity for omissions of information, documentation, or care to be identified and addressed at the commencement of a shift.

Future research

Future studies on the validation of the modified handover model tool in various medical fields, strategies to reinforce the use of the modified handover model tool during all patient-related communication among health care providers, and comparison studies on the modified handover model tool communication tool would be beneficial.

Translation of these findings for enhanced patient safety should be measured in the future, along with sustainability of the new nursing process and external validation of the findings in other settings.

Data availability

The datasets used and/or analysed during the current study are available from the corresponding author upon reasonable request.

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Acknowledgements

This article was derived from a master thesis of aging nursing. The authors would like to acknowledge the research deputy at Babol University of medical sciences for their support.

This study was supported by research deputy at Babol University of medical sciences.

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Fatemeh Mohammadkhah, Ali Pourhabib & Zahra Fotokian

Department of Critical Care Nursing, School of Nursing and Midwifery, Qazvin University of Medical Sciences, Qazvin, Iran

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All authors contributed to the study conception and design, also all authors read and approved the final manuscript. Atefe Alizadeh-riseni, Zahra Fotokian: Study concept and design, Acquisition of subjects and/or data, Analysis and interpretation of data. Fatemeh Mohammadkhah, Ali Pourhabib: Study design, Analysis and interpretation of data, Preparation of manuscript. Marziyeh Khatooni: Analysis and interpretation of data.

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Alizadeh-risani, A., Mohammadkhah, F., Pourhabib, A. et al. Comparison of the SBAR method and modified handover model on handover quality and nurse perception in the emergency department: a quasi-experimental study. BMC Nurs 23 , 585 (2024). https://doi.org/10.1186/s12912-024-02266-4

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Experimental and Quasi-Experimental Designs in Implementation Research

Christopher j. miller.

a VA Boston Healthcare System, Center for Healthcare Organization and Implementation Research (CHOIR), United States Department of Veterans Affairs, Boston, MA, USA

b Department of Psychiatry, Harvard Medical School, Boston, MA, USA

Shawna N. Smith

c Department of Psychiatry, University of Michigan Medical School, Ann Arbor, MI, USA

d Survey Research Center, Institute for Social Research, University of Michigan, Ann Arbor, MI, USA

Marianne Pugatch

Implementation science is focused on maximizing the adoption, appropriate use, and sustainability of effective clinical practices in real world clinical settings. Many implementation science questions can be feasibly answered by fully experimental designs, typically in the form of randomized controlled trials (RCTs). Implementation-focused RCTs, however, usually differ from traditional efficacy- or effectiveness-oriented RCTs on key parameters. Other implementation science questions are more suited to quasi-experimental designs, which are intended to estimate the effect of an intervention in the absence of randomization. These designs include pre-post designs with a non-equivalent control group, interrupted time series (ITS), and stepped wedges, the last of which require all participants to receive the intervention, but in a staggered fashion. In this article we review the use of experimental designs in implementation science, including recent methodological advances for implementation studies. We also review the use of quasi-experimental designs in implementation science, and discuss the strengths and weaknesses of these approaches. This article is therefore meant to be a practical guide for researchers who are interested in selecting the most appropriate study design to answer relevant implementation science questions, and thereby increase the rate at which effective clinical practices are adopted, spread, and sustained.

1. Background

The first documented clinical trial was conducted in 1747 by James Lind, a royal navy physician, who tested the hypothesis that citrus fruit could cure scurvy. Since then, based on foundational work by Fisher and others (1935), the randomized controlled trial (RCT) has emerged as the gold standard for testing the efficacy of treatment versus a control condition for individual patients. Randomization of patients is seen as a crucial to reducing the impact of measured or unmeasured confounding variables, in turn allowing researchers to draw conclusions regarding causality in clinical trials.

As described elsewhere in this special issue, implementation science is ultimately focused on maximizing the adoption, appropriate use, and sustainability of effective clinical practices in real world clinical settings. As such, some implementation science questions may be addressed by experimental designs. For our purposes here, we use the term “experimental” to refer to designs that feature two essential ingredients: first, manipulation of an independent variable; and second, random assignment of subjects. This corresponds to the definition of randomized experiments originally championed by Fisher (1925) . From this perspective, experimental designs usually take the form of RCTs—but implementation- oriented RCTs typically differ in important ways from traditional efficacy- or effectiveness-oriented RCTs. Other implementation science questions require different methodologies entirely: specifically, several forms of quasi-experimental designs may be used for implementation research in situations where an RCT would be inappropriate. These designs are intended to estimate the effect of an intervention despite a lack of randomization. Quasi-experimental designs include pre-post designs with a nonequivalent control group, interrupted time series (ITS), and stepped wedge designs. Stepped wedges are studies in which all participants receive the intervention, but in a staggered fashion. It is important to note that quasi-experimental designs are not unique to implementation science. As we will discuss below, however, each of them has strengths that make them particularly useful in certain implementation science contexts.

Our goal for this manuscript is two-fold. First, we will summarize the use of experimental designs in implementation science. This will include discussion of ways that implementation-focused RCTs may differ from efficacy- or effectiveness-oriented RCTs. Second, we will summarize the use of quasi-experimental designs in implementation research. This will include discussion of the strengths and weaknesses of these types of approaches in answering implementation research questions. For both experimental and quasi-experimental designs, we will discuss a recent implementation study as an illustrative example of one approach.

1. Experimental Designs in Implementation Science

RCTs in implementation science share the same basic structure as efficacy- or effectiveness-oriented RCTs, but typically feature important distinctions. In this section we will start by reviewing key factors that separate implementation RCTs from more traditional efficacy- or effectiveness-oriented RCTs. We will then discuss optimization trials, which are a type of experimental design that is especially useful for certain implementation science questions. We will then briefly turn our attention to single subject experimental designs (SSEDs) and on-off-on (ABA) designs.

The first common difference that sets apart implementation RCTs from more traditional clinical trials is the primary research question they aim to address. For most implementation trials, the primary research question is not the extent to which a particular treatment or evidence-based practice is more effective than a comparison condition, but instead the extent to which a given implementation strategy is more effective than a comparison condition. For more detail on this pivotal issue, see Drs. Bauer and Kirchner in this special issue.

Second, as a corollary of this point, implementation RCTs typically feature different outcome measures than efficacy or effectiveness RCTs, with an emphasis on the extent to which a health intervention was successfully implemented rather than an evaluation of the health effects of that intervention ( Proctor et al., 2011 ). For example, typical implementation outcomes might include the number of patients who receive the intervention, or the number of providers who administer the intervention as intended. A variety of evaluation-oriented implementation frameworks may guide the choices of such measures (e.g. RE-AIM; Gaglio et al., 2013 ; Glasgow et al., 1999 ). Hybrid implementation-effectiveness studies attend to both effectiveness and implementation outcomes ( Curran et al., 2012 ); these designs are also covered in more detail elsewhere in this issue (Landes, this issue).

Third, given their focus, implementation RCTs are frequently cluster-randomized (i.e. with sites or clinics as the unit of randomization, and patients nested within those sites or clinics). For example, consider a hypothetical RCT that aims to evaluate the implementation of a training program for cognitive behavioral therapy (CBT) in community clinics. Randomizing at the patient level for such a trial would be inappropriate due to the risk of contamination, as providers trained in CBT might reasonably be expected to incorporate CBT principles into their treatment even to patients assigned to the control condition. Randomizing at the provider level would also risk contamination, as providers trained in CBT might discuss this treatment approach with their colleagues. Thus, many implementation trials are cluster randomized at the site or clinic level. While such clustering minimizes the risk of contamination, it can unfortunately create commensurate problems with confounding, especially for trials with very few sites to randomize. Stratification may be used to at least partially address confounding issues in cluster- randomized and more traditional trials alike, by ensuring that intervention and control groups are broadly similar on certain key variables. Furthermore, such allocation schemes typically require analytic models that account for this clustering and the resulting correlations among error structures (e.g., generalized estimating equations [GEE] or mixed-effects models; Schildcrout et al., 2018 ).

1.1. Optimization trials

Key research questions in implementation science often involve determining which implementation strategies to provide, to whom, and when, to achieve optimal implementation success. As such, trials designed to evaluate comparative effectiveness, or to optimize provision of different types or intensities of implementation strategies, may be more appealing than traditional effectiveness trials. The methods described in this section are not unique to implementation science, but their application in the context of implementation trials may be particularly useful for informing implementation strategies.

While two-arm RCTs can be used to evaluate comparative effectiveness, trials focused on optimizing implementation support may use alternative experimental designs ( Collins et al., 2005 ; Collins et al., 2007 ). For example, in certain clinical contexts, multi-component “bundles” of implementation strategies may be warranted (e.g. a bundle consisting of clinician training, technical assistance, and audit/feedback to encourage clinicians to use a new evidence-based practice). In these situations, implementation researchers might consider using factorial or fractional-factorial designs. In the context of implementation science, these designs randomize participants (e.g. sites or providers) to different combinations of implementation strategies, and can be used to evaluate the effectiveness of each strategy individually to inform an optimal combination (e.g. Coulton et al., 2009 ; Pellegrini et al., 2014 ; Wyrick, et al., 2014 ). Such designs can be particularly useful in informing multi-component implementation strategies that are not redundant or overly burdensome ( Collins et al., 2014a ; Collins et al., 2009 ; Collins et al., 2007 ).

Researchers interested in optimizing sequences of implementation strategies that adapt to ongoing needs over time may be interested in a variant of factorial designs known as the sequential, multiple-assignment randomized trial (SMART; Almirall et al., 2012 ; Collins et al., 2014b ; Kilbourne et al., 2014b ; Lei et al., 2012 ; Nahum-Shani et al., 2012 ; NeCamp et al., 2017 ). SMARTs are multistage randomized trials in which some or all participants are randomized more than once, often based on ongoing information (e.g., treatment response). In implementation research, SMARTs can inform optimal sequences of implementation strategies to maximize downstream clinical outcomes. Thus, such designs are well-suited to answering questions about what implementation strategies should be used, in what order, to achieve the best outcomes in a given context.

One example of an implementation SMART is the Adaptive Implementation of Effective Program Trial (ADEPT; Kilbourne et al., 2014a ). ADEPT was a clustered SMART ( NeCamp et al., 2017 ) designed to inform an adaptive sequence of implementation strategies for implementing an evidence-based collaborative chronic care model, Life Goals ( Kilbourne et al., 2014c ; Kilbourne et al., 2012a ), into community-based practices. Life Goals, the clinical intervention being implemented, has proven effective at improving physical and mental health outcomes for patients with unipolar and bipolar depression by encouraging providers to instruct patients in self-management, and improving clinical information systems and care management across physical and mental health providers ( Bauer et al., 2006 ; Kilbourne et al., 2012a ; Kilbourne et al., 2008 ; Simon et al., 2006 ). However, in spite of its established clinical effectiveness, community-based clinics experienced a number of barriers in trying to implement the Life Goals model, and there were questions about how best to efficiently and effectively augment implementation strategies for clinics that struggled with implementation.

The ADEPT study was thus designed to determine the best sequence of implementation strategies to offer sites interested in implementing Life Goals. The ADEPT study involved use of three different implementation strategies. First, all sites received implementation support based on Replicating Effective Programs (REP), which offered an implementation manual, brief training, and low- level technical support ( Kilbourne et al., 2007 ; Kilbourne et al., 2012b ; Neumann and Sogolow, 2000 ). REP implementation support had been previously found to be low-cost and readily scalable, but also insufficient for uptake for many community-based settings ( Kilbourne et al., 2015 ). For sites that failed to implement Life Goals under REP, two additional implementation strategies were considered as augmentations to REP: External Facilitation (EF; Kilbourne et al., 2014b ; Stetler et al., 2006 ), consisting of phone-based mentoring in strategic skills from a study team member; and Internal Facilitation (IF; Kirchner et al., 2014 ), which supported protected time for a site employee to address barriers to program adoption.

The ADEPT study was designed to evaluate the best way to augment support for these sites that were not able to implement Life Goals under REP, specifically querying whether it was better to augment REP with EF only or the more intensive EF/IF, and whether augmentations should be provided all at once, or staged. Intervention assignments are mapped in Figure 1 . Seventy-nine community-based clinics across Michigan and Colorado were provided with initial implementation support under REP. After six months, implementation of the clinical intervention, Life Goals, was evaluated at all sites. Sites that had failed to reach an adequate level of delivery (defined as those sites enrolling fewer than ten patients in Life Goals, or those at which fewer than 50% of enrolled patients had received at least three Life Goals sessions) were considered non-responsive to REP and randomized to receive additional support through either EF or combined EF/IF. After six further months, Life Goals implementation at these sites was again evaluated. Sites surpassing the implementation response benchmark had their EF or EF/IF support discontinued. EF/IF sites that remained non-responsive continued to receive EF/IF for an additional six months. EF sites that remained non-responsive were randomized a second time to either continue with EF or further augment with IF. This design thus allowed for comparison of three different adaptive implementation interventions for sites that were initially non-responsive to REP to determine the best adaptive sequence of implementation support for sites that were initially non-responsive under REP:

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SMART design from ADEPT trial.

Provide EF for 6 months; continue EF for a further six months for sites that remain nonresponsive; discontinue EF for sites that are responsive;
Provide EF/IF for 6 months; continue EF/IF for a further six months for sites that remain non-responsive; discontinue EF/IF for sites that are responsive; and
Provide EF for 6 months; step up to EF/IF for a further six months for sites that remain non-responsive; discontinue EF for sites that are responsive.

While analyses of this study are still ongoing, including the comparison of these three adaptive sequences of implementation strategies, results have shown that patients at sites that were randomized to receive EF as the initial augmentation to REP saw more improvement in clinical outcomes (SF-12 mental health quality of life and PHQ-9 depression scores) after 12 months than patients at sites that were randomized to receive the more intensive EF/IF augmentation.

1.2. Single Subject Experimental Designs and On-Off-On (ABA) Designs

We also note that there are a variety of Single Subject Experimental Designs (SSEDs; Byiers et al., 2012 ), including withdrawal designs and alternating treatment designs, that can be used in testing evidence-based practices. Similarly, an implementation strategy may be used to encourage the use of a specific treatment at a particular site, followed by that strategy’s withdrawal and subsequent reinstatement, with data collection throughout the process (on-off-on or ABA design). A weakness of these approaches in the context of implementation science, however, is that they usually require reversibility of the intervention (i.e. that the withdrawal of implementation support truly allows the healthcare system to revert to its pre-implementation state). When this is not the case—for example, if a hypothetical study is focused on training to encourage use of an evidence-based psychotherapy—then these designs may be less useful.

2. Quasi-Experimental Designs in Implementation Science

In some implementation science contexts, policy-makers or administrators may not be willing to have a subset of participating patients or sites randomized to a control condition, especially for high-profile or high-urgency clinical issues. Quasi-experimental designs allow implementation scientists to conduct rigorous studies in these contexts, albeit with certain limitations. We briefly review the characteristics of these designs here; other recent review articles are available for the interested reader (e.g. Handley et al., 2018 ).

2.1. Pre-Post with Non-Equivalent Control Group

The pre-post with non-equivalent control group uses a control group in the absence of randomization. Ideally, the control group is chosen to be as similar to the intervention group as possible (e.g. by matching on factors such as clinic type, patient population, geographic region, etc.). Theoretically, both groups are exposed to the same trends in the environment, making it plausible to decipher if the intervention had an effect. Measurement of both treatment and control conditions classically occurs pre- and post-intervention, with differential improvement between the groups attributed to the intervention. This design is popular due to its practicality, especially if data collection points can be kept to a minimum. It may be especially useful for capitalizing on naturally occurring experiments such as may occur in the context of certain policy initiatives or rollouts—specifically, rollouts in which it is plausible that a control group can be identified. For example, Kirchner and colleagues (2014) used this type of design to evaluate the integration of mental health services into primary care clinics at seven US Department of Veterans Affairs (VA) medical centers and seven matched controls.

One overarching drawback of this design is that it is especially vulnerable to threats to internal validity ( Shadish, 2002 ), because pre-existing differences between the treatment and control group could erroneously be attributed to the intervention. While unmeasured differences between treatment and control groups are always a possibility in healthcare research, such differences are especially likely to occur in the context of these designs due to the lack of randomization. Similarly, this design is particularly sensitive to secular trends that may differentially affect the treatment and control groups ( Cousins et al., 2014 ; Pape et al., 2013 ), as well as regression to the mean confounding study results ( Morton and Torgerson, 2003 ). For example, if a study site is selected for the experimental condition precisely because it is underperforming in some way, then regression to the mean would suggest that the site will show improvement regardless of any intervention; in the context of a pre-post with non-equivalent control group study, however, this improvement would erroneously be attributed to the intervention itself (Type I error).

There are, however, various ways that implementation scientists can mitigate these weaknesses. First, as mentioned briefly above, it is important to select a control group that is as similar as possible to the intervention site(s), which can include matching at both the health care network and clinic level (e.g. Kirchner et al., 2014 ). Second, propensity score weighting (e.g. Morgan, 2018 ) can statistically mitigate internal validity concerns, although this approach may be of limited utility when comparing secular trends between different study cohorts ( Dimick and Ryan, 2014 ). More broadly, qualitative methods (e.g. periodic interviews with staff at intervention and control sites) can help uncover key contextual factors that may be affecting study results above and beyond the intervention itself.

2.2. Interrupted Time Series

Interrupted time series (ITS; Shadish, 2002 ; Taljaard et al., 2014 ; Wagner et al., 2002 ) designs represent one of the most robust categories of quasi-experimental designs. Rather than relying on a non-equivalent control group, ITS designs rely on repeated data collections from intervention sites to determine whether a particular intervention is associated with improvement on a given metric relative to the pre-intervention secular trend. They are particularly useful in cases where a comparable control group cannot be identified—for example, following widespread implementation of policy mandates, quality improvement initiatives, or dissemination campaigns ( Eccles et al., 2003 ). In ITS designs, data are collected at multiple time points both before and after an intervention (e.g., policy change, implementation effort), and analyses explore whether the intervention was associated with the outcome beyond any pre-existing secular trend. More formally, ITS evaluations focus on identifying whether there is discontinuity in the trend (change in slope or level) after the intervention relative to before the intervention, using segmented regression to model pre- and post-intervention trends ( Gebski et al., 2012 ; Penfold and Zhang, 2013 ; Taljaard et al., 2014 ; Wagner et al., 2002 ). A number of recent implementation studies have used ITS designs, including an evaluation of implementation of a comprehensive smoke-free policy in a large UK mental health organization to reduce physical assaults ( Robson et al., 2017 ); the impact of a national policy limiting alcohol availability on suicide mortality in Slovenia ( Pridemore and Snowden, 2009 ); and the effect of delivery of a tailored intervention for primary care providers to increase psychological referrals for women with mild to moderate postnatal depression ( Hanbury et al., 2013 ).

ITS designs are appealing in implementation work for several reasons. Relative to uncontrolled pre-post analyses, ITS analyses reduce the chances that intervention effects are confounded by secular trends ( Bernal et al., 2017 ; Eccles et al., 2003 ). Time-varying confounders, such as seasonality, can also be adjusted for, provided adequate data ( Bernal et al., 2017 ). Indeed, recent work has confirmed that ITS designs can yield effect estimates similar to those derived from cluster-randomized RCTs ( Fretheim et al., 2013 ; Fretheim et al., 2015 ). Relative to an RCT, ITS designs can also allow for a more comprehensive assessment of the longitudinal effects of an intervention (positive or negative), as effects can be traced over all included time points ( Bernal et al., 2017 ; Penfold and Zhang, 2013 ).

ITS designs also present a number of challenges. First, the segmented regression approach requires clear delineation between pre- and post-intervention periods; interventions with indeterminate implementation periods are likely not good candidates for ITS. While ITS designs that include multiple ‘interruptions’ (e.g. introductions of new treatment components) are possible, they will require collection of enough time points between interruptions to ensure that each intervention’s effects can be ascertained individually ( Bernal et al., 2017 ). Second, collecting data from sufficient time points across all sites of interest, especially for the pre-intervention period, can be challenging ( Eccles et al., 2003 ): a common recommendation is at least eight time points both pre- and post-intervention ( Penfold and Zhang, 2013 ). This may be onerous, particularly if the data are not routinely collected by the health system(s) under study. Third, ITS cannot protect against confounding effects from other interventions that begin contemporaneously and may impact similar outcomes ( Eccles et al., 2003 ).

2.3. Stepped Wedge Designs

Stepped wedge trials are another type of quasi-experimental design. In a stepped wedge, all participants receive the intervention, but are assigned to the timing of the intervention in a staggered fashion ( Betran et al., 2018 ; Brown and Lilford, 2006 ; Hussey and Hughes, 2007 ), typically at the site or cluster level. Stepped wedge designs have their analytic roots in balanced incomplete block designs, in which all pairs of treatments occur an equal number of times within each block ( Hanani, 1961 ). Traditionally, all sites in stepped wedge trials have outcome measures assessed at all time points, thus allowing sites that receive the intervention later in the trial to essentially serve as controls for early intervention sites. A recent special issue of the journal Trials includes more detail on these designs ( Davey et al., 2015 ), which may be ideal for situations in which it is important for all participating patients or sites to receive the intervention during the trial. Stepped wedge trials may also be useful when resources are scarce enough that intervening at all sites at once (or even half of the sites as in a standard treatment-versus-control RCT) would not be feasible. If desired, the administration of the intervention to sites in waves allows for lessons learned in early sites to be applied to later sites (via formative evaluation; see Elwy et al., this issue).

The Behavioral Health Interdisciplinary Program (BHIP) Enhancement Project is a recent example of a stepped-wedge implementation trial ( Bauer et al., 2016 ; Bauer et al., 2019 ). This study involved using blended facilitation (including internal and external facilitators; Kirchner et al., 2014 ) to implement care practices consistent with the collaborative chronic care model (CCM; Bodenheimer et al., 2002a , b ; Wagner et al., 1996 ) in nine outpatient mental health teams in VA medical centers. Figure 2 illustrates the implementation and stepdown periods for that trial, with black dots representing primary data collection points.

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BHIP Enhancement Project stepped wedge (adapted form Bauer et al., 2019).

The BHIP Enhancement Project was conducted as a stepped wedge for several reasons. First, the stepped wedge design allowed the trial to reach nine sites despite limited implementation resources (i.e. intervening at all nine sites simultaneously would not have been feasible given study funding). Second, the stepped wedge design aided in recruitment and retention, as all participating sites were certain to receive implementation support during the trial: at worst, sites that were randomized to later- phase implementation had to endure waiting periods totaling about eight months before implementation began. This was seen as a major strength of the design by its operational partner, the VA Office of Mental Health and Suicide Prevention. To keep sites engaged during the waiting period, the BHIP Enhancement Project offered a guiding workbook and monthly technical support conference calls.

Three additional features of the BHIP Enhancement Project deserve special attention. First, data collection for late-implementing sites did not begin until immediately before the onset of implementation support (see Figure 2 ). While this reduced statistical power, it also significantly reduced data collection burden on the study team. Second, onset of implementation support was staggered such that wave 2 began at the end of month 4 rather than month 6. This had two benefits: first, this compressed the overall amount of time required for implementation during the trial. Second, it meant that the study team only had to collect data from one site at a time, with data collection periods coming every 2–4 months. More traditional stepped wedge approaches typically have data collection across sites temporally aligned (e.g. Betran et al., 2018 ). Third, the BHIP Enhancement Project used a balancing algorithm ( Lew et al., 2019 ) to assign sites to waves, retaining some of the benefits of randomization while ensuring balance on key site characteristics (e.g. size, geographic region).

Despite their utility, stepped wedges have some important limitations. First, because they feature delayed implementation at some sites, stepped wedges typically take longer than similarly-sized parallel group RCTs. This increases the chances that secular trends, policy changes, or other external forces impact study results. Second, as with RCTs, imbalanced site assignment can confound results. This may occur deliberately in some cases—for example, if sites that develop their implementation plans first are assigned to earlier waves. Even if sites are randomized, however, early and late wave sites may still differ on important characteristics such as size, rurality, and case mix. The resulting confounding between site assignment and time can threaten the internal validity of the study—although, as above, balancing algorithms can reduce this risk. Third, the use of formative evaluation (Elwy, this issue), while useful for maximizing the utility of implementation efforts in a stepped wedge, can mean that late-wave sites receive different implementation strategies than early-wave sites. Similarly, formative evaluation may inform midstream adaptations to the clinical innovation being implemented. In either case, these changes may again threaten internal validity. Overall, then, stepped wedges represent useful tools for evaluating the impact of health interventions that (as with all designs) are subject to certain weaknesses and limitations.

3. Conclusions and Future Directions

Implementation science is focused on maximizing the extent to which effective healthcare practices are adopted, used, and sustained by clinicians, hospitals, and systems. Answering questions in these domains frequently requires different research methods than those employed in traditional efficacy- or effectiveness-oriented randomized clinical trials (RCTs). Implementation-oriented RCTs typically feature cluster or site-level randomization, and emphasize implementation outcomes (e.g. the number of patients receiving the new treatment as intended) rather than traditional clinical outcomes. Hybrid implementation-effectiveness designs incorporate both types of outcomes; more details on these approaches can be found elsewhere in this special issue (Landes, this issue). Other methodological innovations, such as factorial designs or sequential, multiple-assignment randomized trials (SMARTs), can address questions about multi-component or adaptive interventions, still under the umbrella of experimental designs. These types of trials may be especially important for demystifying the “black box” of implementation—that is, determining what components of an implementation strategy are most strongly associated with implementation success. In contrast, pre-post designs with non-equivalent control groups, interrupted time series (ITS), and stepped wedge designs are all examples of quasiexperimental designs that may serve implementation researchers when experimental designs would be inappropriate. A major theme cutting across each of these designs is that there are relative strengths and weaknesses associated with any study design decision. Determining what design to use ultimately will need to be informed by the primary research question to be answered, while simultaneously balancing the need for internal validity, external validity, feasibility, and ethics.

New innovations in study design are constantly being developed and refined. Several such innovations are covered in other articles within this special issue (e.g. Kim et al., this issue). One future direction relevant to the study designs presented in this article is the potential for adaptive trial designs, which allow information gleaned during the trial to inform the adaptation of components like treatment allocation, sample size, or study recruitment in the later phases of the same trial ( Pallmann et al., 2018 ). These designs are becoming increasingly popular in clinical treatment ( Bhatt and Mehta, 2016 ) but could also hold promise for implementation scientists, especially as interest grows in rapid-cycle testing of implementation strategies or efforts. Adaptive designs could potentially be incorporated into both SMART designs and stepped wedge studies, as well as traditional RCTs to further advance implementation science ( Cheung et al., 2015 ). Ideally, these and other innovations will provide researchers with increasingly robust and useful methodologies for answering timely implementation science questions.

Many implementation science questions can be addressed by fully experimental designs (e.g. randomized controlled trials [RCTs]).
Implementation trials differ in important ways, however, from more traditional efficacy- or effectiveness-oriented RCTs.
Adaptive designs represent a recent innovation to determine optimal implementation strategies within a fully experimental framework.
Quasi-experimental designs can be used to answer implementation science questions in the absence of randomization.
The choice of study designs in implementation science requires careful consideration of scientific, pragmatic, and ethical issues.

Acknowledgments

This work was supported by Department of Veterans Affairs grants QUE 15–289 (PI: Bauer) and CIN 13403 and National Institutes of Health grant RO1 MH 099898 (PI: Kilbourne).

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Iztok Tiselj ORCID: orcid.org/0000-0001-9340-5397 1 , 2 ,
Jan Kren 1 , 2 ,
Blaž Mikuž 1 ,
Raksmy Nop 3 ,
Alan Burlot 3 &
Grégoire Hamrit 3

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The stagnant Taylor bubble in vertical isothermal turbulent counter-current flow was analyzed using 2D shadowgraphy experiments and two distinct high-fidelity numerical simulations. One simulation employed the geometrical VOF interface tracking method within the OpenFOAM code, while the other utilized the explicit front tracking method of the TrioCFD code. Interface recognition algorithms were applied to the photographs and compared with the results of 3D simulations performed with LES and pseudo-DNS accuracy in OpenFOAM and TrioCFD, respectively. The measured Taylor bubbles exhibited an asymmetric bullet-train shape and a specific speed, which were compared with the predictions of both numerical approaches. Reproducing the experiment proved challenging for both otherwise well-established methods frequently used in interface tracking simulations of two-phase flows. Grid resolution and subgrid turbulent models, known for their success in single-phase turbulence, were less accurate near the water–air interface. Additional experimental parameters compared with simulations were related to the dynamics of tiny disturbance waves with amplitudes ranging from 10 to 100 µm along the interface of the Taylor bubbles. The speed and spectra of the surface disturbance waves were reproduced numerically with moderate success despite detailed grid refinement in the relevant region of the computational domain.

Taylor Bubble Dynamics in Pipe Fittings: A Numerical Study

Pressure drop and bubble velocity in Taylor flow through square microchannel

Taylor Bubbles in Small Channels: A Proper Guiding Measure for Validation of Numerical Methods for Interface Resolving Simulations

Avoid common mistakes on your manuscript.

1 Introduction

Gas–liquid mixture flows exhibit various two-phase flow patterns, with vertical pipes commonly experiencing bubbly, slug, churn, annular, and droplet flow regimes [ 1 ]. The specific flow regime depends on factors such as flow velocities, phase volume fractions, fluid properties, pipe size, and orientation. This study is focused on Taylor bubble flow, which falls under the slug flow regime. Taylor bubbles are bullet-shaped bubbles that move at different speeds from the bulk liquid, occupying almost the entire pipe cross section. Slug flows are relevant for chemical, nuclear, petroleum, and other types of processing engineering. They are encountered in a wide range of practical applications, including vaporizers, boilers, filtration and membrane processes [ 2 ], as well as extreme events in the petroleum industry [ 3 ] or steam generators in nuclear power plants. The most recent review paper discussing vertical gas–liquid slug flows by Holagh & Ahmed from 2024 [ 4 ] demonstrates the extensive scope of this research area. This remarkable review is citing 470 references.

The type of slug flows relevant to the present study occurs in the inertia-dominant regime, where the influence of viscosity and surface tension is minimal [ 1 ]. In this regime, the drift velocity of Taylor bubbles \({U}_{0}\) in pipe with diameter D is given by the correlation \({U}_{0}=k\sqrt{gD}\) ( g acceleration of gravity). Based on the constant value of k ≈0.35, this correlation predicts a drift velocity of approximately 0.18 m/s for Taylor bubbles in our experiments [ 5 ]. This value is close to the average measured liquid velocity, \({U}_{L}\) , which is in the downward direction (negative sign) and keeps the bubble fixed in position. Dumitrescu [ 6 ] demonstrated that soon after the liquid flow was directed downward, the Taylor bubble became unstable. One of the earliest detailed experiments on counter-current turbulent flow was performed by Martin [ 7 ], who studied air–water mixtures in circular pipes with diameters of 2.6, 10.16, and 14.0 cm. Martin found that the bubble velocity in counter-current slug flow could not be adequately explained by existing theories for co-current background flow or stagnant liquid conditions. This discrepancy is due to bubble instability, which increases bubble velocity when the bubble is displaced from the pipe axis. Lu and Prosperetti [ 8 ] performed a stability analysis and showed that the breakup of Taylor bubble symmetry occurs at liquid velocities below a critical negative velocity of \({U}_{c}=-0.13\sqrt{gD}\) . Figueroa-Espinoza and Fabre [ 9 ] performed numerical analyses of symmetry breakup at different surface tension values. They found that asymmetry leads to increased bubble velocity and a decreased curvature radius at the stagnation point of the bubble nose. Fabre and Figueroa-Espinoza [ 10 ] further investigated symmetry breakup experimentally and determined that asymmetry is largely independent of whether the flow regime is turbulent or laminar. They identified the vorticity-to-radius ratio at the stagnation point as a crucial parameter for symmetry breakup. Fershtman et al. [ 11 ] also studied counter-current slug flow, measuring a liquid velocity that exactly balances buoyancy \({U}_{L}=0.35\sqrt{gD}\) = 0.178 m/s, which was also observed in experiments in the present study. The latest study by Abubakar and Matar [ 12 ] provided a detailed numerical and parametric analysis of the effects of downward liquid velocity, viscosity, and surface tension on bubble shape and motion. Their linear stability analysis identified regions of dimensionless parameters where the bubble is unstable and assumes an asymmetric shape, and they explained the mechanisms behind symmetry breakup. Our experiments were conducted in the unstable region with asymmetric bubble shapes, necessitating dynamic flow rate control, as described in the following section.

The interactions between Taylor bubbles and turbulent liquid flow have been the subject of various studies. Unlike in laminar liquid flow, the tail of the bubble starts to break in the turbulent background flow. The breakup and recoalescence processes in the bubble wake region have been observed. The studies [ 13 , 14 ] measured the gas loss from a stationary Taylor bubble in a counter-current liquid flow using a special spherical Teflon cap to hold the bubble in a fixed position. More recent experiments involving the turbulent counter-current regime have utilized high-speed cameras in visible light to measure the bubble’s disintegration rate [ 15 ]. They have shown that disintegration by the breakup stops when the Taylor bubble is sufficiently short. This result is important for the present study focused on the Taylor bubbles, which do not lose their mass due to the breakup of the bubble’s tail. As shown in [ 15 , 37 ], even shorter bubbles are gradually losing their mass due to the dissolving of the gas in the liquid. However, this mechanism is much slower than the physical breakup and can be neglected over the time intervals relevant for the present study. Consequently, dynamical control of the liquid flow rate is used to trap the bubble in an equilibrium position for hours, and allowing for studies over several minutes.

Two fundamentally different approaches are used for numerical simulations of turbulent two-phase flows:

One approach is the Euler-Euler method, wherein the Navier–Stokes equations are solved independently for each phase [ 16 ].

Another approach is the one-fluid formulation, which involves applying a single set of governing equations across the entire domain, encompassing the interface [ 17 ]. Various methods for interface advection exist, with the Volume of Fluid (VOF) method [ 19 , 20 ], Front tracking method [ 21 ], and Level-Set method [ 30 ] being among the most widely used. The present research is focused on the (VOF) method and on the Front tracking method, which were tested with the stagnant Taylor bubble in turbulent flow.

The specific version of the VOF method used in this study is implemented in the open-source OpenFOAM computer code [ 18 ]. One of the main advantages of the VOF method over alternative methods is its well-established framework and guaranteed volume conservation. Central to the VOF method is the concept of a marker function, which represents the volume fraction of one fluid within each computational cell of the domain. A key challenge in advecting a marker function is the numerical diffusion that arises from using a cell-averaged marker function [ 21 ]. To mitigate this diffusion, the VOF method reconstructs the interface so that the marker does not move into a new cell until the current cell is completely filled. Reconstruction models of the VOF method are categorized into algebraic and geometric types. Significant effort has been focused on geometric methods because they produce better results than algebraic reconstruction methods [ 23 , 24 ]. One such geometric method is the piecewise linear interface calculation (PLIC) method, which has been investigated for large eddy simulations (LES) by Kren et al. [ 22 ] and is tested in the present paper. Large eddy simulation (LES) is a very useful compromise between the high accuracy and cost of direct numerical simulation (DNS) and the lower cost but reduced accuracy of Reynolds-averaged Navier–Stokes (RANS) simulations. The development of LES methods for multiphase flows is still in its early stages, largely due to the lack of experimental and DNS benchmarks. Klein et al. [ 25 ] have laid out a framework for developing LES in multiphase flows. In single-phase flows, modeling small scales is required only for the convective term, typically achieved by adding eddy viscosity to the equations. However, multiphase flows require modeling several terms, with at least two being particularly significant. While the convective term can be approached in a similar manner to single-phase flows [ 26 ], new models are needed for other closures. Recent developments highlight that the closure of the sub-grid term for surface tension is the most critical [ 22 ].

Numerical simulations of multiphase flows using the front-tracking method have been presented by Unverdi in 1992 [ 27 ] and upgraded by Tryggvason et al. [ 28 ]. Like in the VOF method, interfacial terms are incorporated by adding the appropriate sources as delta functions at the phase boundaries. The unsteady Navier–Stokes equations are solved using a conventional finite volume or finite element method on a fixed, structured grid. The interface, or front, is explicitly tracked using connected marker points in Lagrangian coordinates, with surfaces in the 3D domain. This type of method is implemented in TrioCFD code [ 35 ], which was the second type of numerical model tested with the stagnant Taylor bubble in turbulent flow. Interfacial source terms such as surface tension are computed on the front and transferred to the fixed grid. The advection of fluid properties, like density, is handled by following the motion of the front. When large topology changes occur, the distance between marker points can increase or decrease, leading to reduced accuracy. To address this, new marker points might be added where marker density is low, and some marker points are removed where density is high. Although the method is complex to implement, it provides highly accurate tracking of the interface position. However, interface breakup does not occur well unless a special model is implemented.

Existing numerical simulations of Taylor bubbles have predominantly focused on stagnant or co-current background liquid flows across various setups, ranging from simplistic 2D and Euler-Euler simulations [ 31 , 32 ] to comprehensive 3D simulations with interface tracking [ 33 , 34 ]. LES investigations of Taylor bubbles within co-current turbulent regimes, without special sub-grid scale models for bubble coalescence or breakup, revealed disintegration rates one to two orders of magnitude faster than observed in experiments of Taylor bubbles within counter-current turbulent flow [ 22 , 36 ].

The present study aims to address details of the Taylor bubble’s interface dynamics in the region of the liquid film and the capabilities of state-of-the art numerical schemes to describe the flow of the thin liquid film and the velocity fields in the liquid and air phase around the interface. An important part of the current work is the study of interface waves: as discussed below, accurate measurements of these waves were performed despite their tiny amplitudes. Consequently, we have examined properties of the interface waves predicted by the OpenFOAM and TrioCFD codes. All instances of waves are traveling fluid oscillations sustained by the surface tension force. For experimental Taylor bubble the interface waves were studied by Kren et al. [ 24 ]. The work on the interfacial waves analysis spans beyond the films of Taylor bubbles: closely related interfacial waves are observed in vertical annular flows, where a recent review is available [ 39 ] and a more specific example by Tekavčič et. al. [ 38 ] who analyzed interfacial waves in water–air churn flow regime. Another slightly less relevant area are studies of horizontally stratified flows with the presence of capillary waves, where some of the recent activities can be found in [ 40 , 41 ].

The goal of the present study is a detailed analysis of one specific experimental case performed within the experimental campaign [ 37 ], where stagnant Taylor bubbles were observed in the counter-current turbulent flow of water. The selected experimental case is reproduced with two state-of-the-art interface tracking approaches capable to operate in turbulent flow regime. Comparison of all measured parameters is performed: the main integral parameter is mass flow rate of the water that is balancing the buoyancy; flow rate is closely related to the axially asymmetric shape of the bubble, which is influencing the bubble drag. The last test is a comparison of the measured and computed interfacial waves that are traveling over the body of the Taylor bubble.

2 Experimental Setup

Experiments were conducted in a loop, as depicted in Fig. 1 . The test section consisted of a 1.5 m long glass pipe with an internal diameter of D = 26 mm and wall thickness 2 mm. Water is entering the test section from the top. All experimental cases, including the one considered in the present paper, were performed in the turbulent flow regime of the liquid above the bubble, with a Reynolds number of approximately 5600. The straight section of the pipe above the bubble spanned around 40 pipe diameters, ensuring statistically uniform turbulence impinging on the bubble. To maintain a constant water temperature of 30 °C, a heat exchanger was utilized in the tank. The Taylor bubble was injected into the test section with a syringe through a small dedicated connection beneath the test section. The flow through the test section was regulated using a control valve, which adjusted the flow distribution between the main loop and a bypass loop.

Schematics of the test loop

Observations of the Taylor bubble were carried out using a high-speed camera (camera Phantom v 1212, objective: TOKINA AT-X PRO D 100 mm), set up at a distance of around 30 cm between the objective and the pipe axis, with a field of view covering a 14 cm (~ 5 diameters) section of the pipe. The pipe was immersed in a rectangular glass section filled with water to minimize optical distortion. The observed Taylor bubbles typically had lengths ranging from 1.5 to 5 pipe diameters. Measurements were performed over different time intervals of 8, 4, 2, and 1 min, with camera frequencies of 100, 200, 400, and 800 Hz, respectively. Around 90 mm long bubble filmed over two minutes interval at frequency 400 Hz was used for detailed analyses in the present study.

The camera’s useful resolution for the measurements was approximately 1280 × 240 pixels, corresponding to around 9 pixels per millimeter. The measurement of absolute liquid film thickness is achieved with a precision ranging between 0.5 and 1 pixel. However, this level of precision introduces relative errors exceeding 40% for very thin films below 3 pixels. The estimated optical distortion, due to the light refraction, results in a maximum enlargement of the liquid film thickness by up to 2%. This value is significantly lower than the uncertainty associated with interface reconstruction.

Each experimental run was performed in the following steps:

Preparation of the water loop, establishment of the water circulation with an expected mass flow rate.

Set-up of the camera, illumination, pressure, temperature and mass flow rate sensors.

Injection of the air bubble.

Fine-tuning of the water mass flow rate to bring the bubble into the camera’s view.

Start of measurements and active fine-tuning of the mass flow rate during the measurement.

Data (image) processing.

In the counter-current flow configuration, the instability of the Taylor bubble requires dynamic adjustments of the mass flow rates during the experiment to ensure that the bubble remains within the camera’s field of view. Minor corrections of the valve position are made every few seconds, leading to fluctuations in the bulk liquid velocity within the test section. The bulk liquid velocity is based on the readings from the Coriolis flow meter, which measures mass flow rate through the section at a frequency of 1 Hz. The variations in the mean velocity measurement due to manual mass flow rate corrections range between 3 and 10% of the bulk velocity across various experimental cases. In analysis of the results these minor changes in the bubble position were considered with a sliding coordinate system which was fixed to the tip of the Taylor bubble’s nose, while the dynamics of the Taylor bubble was practically unaffected by the mass flow rate changes. As shown in [ 37 ] the bubbles moved up and down with vertical velocities below 0.01 m/s, which were considerably lower than the upstream mean liquid velocity of 0.18 m/s and the velocities around 1 m/s observed on the liquid–air interface of the bubble. While the system of bubble position control may present challenges when comparing results with similar experiments or numerical simulations, it closely resembles the numerical technique employed in high-fidelity simulations of co-current Taylor bubble flow [ 45 , 46 ]. In these simulations, the Taylor bubble is modeled within a moving frame of reference to ensure the bubble remains inside the computational domain. The same approach was used in TrioCFD simulation in this paper, while the adaptive mass flow rate boundary condition was used in the OpenFOAM.

The processing of each recording involved analyzing a set of 50,000 photographs using a dedicated in-house software. The best scaling distance on the photographs turned out to be the outer diameter of the glass pipe, which is not affected by the optical distortion. This software utilized widely used libraries for tasks such as fitting two-dimensional surfaces and one-dimensional lines, performing Fourier transformations, and cross-correlating one-dimensional functions. The algorithms and techniques employed in the software were based on methods described in the Numerical Recipes book [ 47 ]. The main focus of the computer codes was image processing, specifically the extraction of the Taylor bubble surface from the images. Given the constraints of automated analysis on a large dataset, we used established image processing methods found in the open literature [ 48 ]. In order to handle the large number of photographs, manual corrections and artifact removal were limited. To address this, a robust procedure was developed that could identify potential failures in bubble interface reconstruction. A description of the algorithm can be found in [ 37 ], while the intermediate results of the particular step of silhouette reconstruction are shown in Fig. 2 :

a = > b: conversion of image density matrix into gradient matrix.

b = > c: identification of the bubble outer surface

c = > d: sub-pixel interface position refinement.

a original image, b magnitude of the gradients field (step 1), c extracted bubble interface and pipe inner walls at pixel level (step 2), d) refinement of the interface position at subpixel level (step 3) with pixel grid in the background: “ + ”—pixel level interface, “x”—sub-pixel level interface. All units in pixels

Distinguishing between absolute and relative accuracy is crucial when considering interface recognition. The absolute uncertainty of the interface position on a single photograph ranges from half a pixel to one pixel. However, when analyzing a time series or spatial profiles of the interface, the relative uncertainty of the interface motion between neighboring pixels in space or time is reduced by a factor of approximately 5 to around ± 0.1 pixel. This improvement in relative accuracy allows very precise characterization of interface movements.

3 Numerical methods

Modeling of the Taylor bubble in the counter-current turbulent flow was performed with two highly accurate but fundamentally rather different approaches (Table 1 ):

The Front tracking method is implemented in TrioCFD code [ 35 ]. The interface position is tracked with a Lagrangian mesh which is advected by the flow. Such an approach allows very accurate interface recognition and dynamics as the interface has a zero thickness; however, it means more expensive numerical algorithm.

The geometric VOF method implemented in the finite volume code OpenFOAM [22] introduces high-order interface capturing scheme, which consists of two parts—interface advection using void fraction property \(\alpha\) and interface reconstruction with different submodels of the VOF method. Computing time of this approach turns out to be shorter, but slightly less accurate in modeling the interface dynamics and surface tension effects.

3.1 Front Tracking in TrioCFD

TRUST/TrioCFD is an open-source CFD code developed by the CEA (the French Atomic Energy and Alternative Energies Commission). Massively parallel, it can handle various physical situations: single or two-phase flow, chemistry, fluid–structure interaction… To model a two-phase flow, one of the possible approaches of TrioCFD is to use its front-tracking method. The latter uses an Euler–Lagrange approach coupled with a Volume-of-Fluid like method. It uses the one-fluid formulation for the fluid problem and an explicit interface tracking by considering:

The indicator function χ k equals 1 in the phase k and 0 otherwise,

The variable \({\phi }_{k}\) (velocity, pressure, density…) having its given value in the phase k .

One can define a one-fluid variable as \(\phi = {\sum }_{k}{\chi }_{k}{\phi }_{k}\) . By summing the continuity equation for incompressible flows, the Navier–Stokes equation for each phase and the Laplace pressure law at the interface, one can derive the equation system:

with \(\overrightarrow{u}\) the velocity field, ρ the density, μ the dynamic viscosity, \(\overrightarrow{g}\) the gravity field, \(\sigma\) the surface tension at the interface, \(\kappa\) the local curvature of the interface \({\delta }_{I}\) the indicator function of the interface and \(\overrightarrow{n}\) the vector normal to the interface. The system of Eq. ( 1 ) is the one-fluid problem solved for the fluid mixture in the front-tracking of TrioCFD. The choice was made to use a non-conservative discrete surface tension rather than a classic Continuum Surface Force model as the latter introduces parasitic currents. The non-conservative effect has been studied and is found negligible [ 29 ].

Regarding the interface (Fig. 3 ), the Lagrangian mesh is advected between two time steps by the velocity field with simple advection equation applied to all Lagrangian markers on the interface \(i=1,N\) :

where \({\overrightarrow{s}}_{\text{i}}\) denotes position of the Lagrangian marker i, and \(\overrightarrow{u}({\overrightarrow{s}}_{\text{i}})\) represents the velocity at the marker position. To ensure the mass conservation, the transport of the phase indicator function with a calculation of the volume of gas is performed to refine the position of the Lagrangian markers. The interface treatment ends by a smoothing and a remeshing to regularize the markers position.

Illustration of the Lagrangian mesh tracking the interface in TrioCFD

In this investigation, an explicit Euler scheme was used for the time integration. Regarding the space discretization, we used the Finite Element Volume method, which is a hybrid between the finite volume and the finite element methods.

As illustrated in Fig. 4 the computational domain is a vertical circular pipe with a length of L = 23 cm and a diameter corresponding to the experimental pipe. At the outlet, a free pressure condition was implemented and at the pipe wall, a no-slip condition was imposed. Fixed mass flow rate was prescribed at the inlet ( v 0 = 0.17 m/s) and the moving frame of reference approach was used in TrioCFD simulation.

Left: scheme of the computational model. Right: cross section of the mesh

As the inlet flow is turbulent, a synthetic turbulence developing an isotropic and homogeneous turbulence was chosen as a boundary condition. The values of turbulent kinetic energy \(k\) and turbulent dissipation rate \(\varepsilon\) on inlet were computed with a preliminary RANS standard k-ε computation. Even though this does not exactly mimic the conditions in a pipe, this approach combined with a certain development length above the bubble head provides satisfactory results and a reasonable computational cost. Let us note that this branching between the synthetic turbulence and the two-phase domain significantly increases the computational time compared to simulations of Taylor bubbles performed with a laminar inlet condition showing excellent results [ 42 ]. Future development to optimize the process is ongoing.

The bubble is initiated as a hemisphere at the head, contiguous to a cylinder of a same radius letting a liquid film of a thickness δ chosen as 2.6 mm (10% of the diameter). This is significantly thicker than the final film thickness but it eases the initialization of the computation. To avoid the bubble to break during the initialization because of the fluid forces, two techniques were used:

The surface tension of the bubble was initiated with a value ten times higher than the physical one, then linearly decreased to its physical value during 0.1 s.

Three zones of uniform velocity were set to avoid excessive initial fluid force: no velocity in the bubble, higher velocity around the bubble, and nominal velocity in the rest of the domain.

The computational domain was meshed using the internal mesh generator of TRUST/TrioCFD coupled with GMSH. The process starts with meshing a quarter of disk in two different sections:

a corona filled with prisms whose size follows a geometrical expansion law. The latter are then cut to triangles.

the bulk domain homogeneously filled with triangles.

The resulted mesh is then extended to generate the mesh of the circular cross section (see Fig. 4 ) and then extruded to produce the entire pipe. The final mesh for TrioCFD simulation constituted of about 2.8 million tetrahedral elements. Details of the mesh characteristics can be found in Table 2 , η being the Kolmogorov length scale computed as η = ν 3/4 ε −1/4 with ν the liquid kinematic viscosity and ε the turbulent dissipation rate, itself estimated with the turbulent length scale approach. The subgrid turbulent model was not used, which means that the code worked with a so-called quasi-DNS approach: mesh was too coarse for DNS but sufficiently fine to allow simulations without turbulent diffusivity.

The length of the bubble after the initial non-physical interval of 0.1 s, was established at around 70 mm. Time interval of the observation was 1 s and the computation took 45,000 CPU-hours on 128 CPU cores.

3.2 Geometric VOF interface tracking in OpenFOAM

A two-phase gas–liquid system has been modeled using the one-fluid formulation of the Navier–Stokes Eqs. ( 1 ) and the geometric VOF approach for interface capturing. Within the VOF framework, a void fraction, denoted as \(\alpha\) , is defined. Its advection equation is given as:

Solution of this equation represents the starting point for the VOF reconstruction of the interface. It is important to emphasize that interface treatment with Lagrangian markers in Eq. ( 2 ) and through the volume fraction advection Eq. ( 3 ) is the key difference between both numerical models used in the present study.

In this computational study, the OpenFOAM v10 software, a widely recognized tool in the field of computational fluid dynamics (CFD), is employed to solve the relevant equations. The core of the simulation is a highly sophisticated and modified interFoam solver. This solver is notable for its capability to utilize diagonally implicit Runge–Kutta (DIRK) time integration schemes, seamlessly integrated with the piecewise linear interface calculation (PLIC) for geometric reconstruction of interfaces. This solver is an advanced iteration of an original version developed in OpenFOAM v4 by Frederix et al. [ 45 ], which was later refined by Kren et al. [ 22 ].

For modeling the subgrid-scale phenomena, the study adopts the Wall-Adapting Local Eddy-viscosity (WALE) model. This eddy viscosity model is particularly effective in capturing the dynamics of turbulent flows at smaller scales. The computational strategy includes the use of the Pressure-Implicit with Splitting of Operators (PISO) algorithm. This algorithm plays a pivotal role in the computational process, as it adeptly decouples the pressure and velocity equations, allowing for their segregated solution. A notable feature of this methodology is the incorporation of two inner corrector loops. This design implies that the pressure equation is reformulated and resolved twice within each stage of the Runge–Kutta (RK) time-stepping process.

Surface tension, a crucial aspect in multi-phase flow simulations, is computed using the continuum surface force (CSF) model [ 51 ]. This model effectively distributes the surface tension force across several computational cells, utilizing a Dirac delta function. To enhance the accuracy of this approach, the Dirac-delta function in the surface tension term is smoothened via the α function. The primary objective of this modeling technique is to precisely equilibrate the forces due to pressure gradients and surface tension, ensuring accurate representation of the physical phenomena in the simulated fluid system. For the spatial discretization of the divergence terms, the finite volume framework was used, which eventually reduces to a simple summation of all the face-normal fluxes across all the faces enclosing each control volume. Similarly to Kren et al. [ 22 ], a blended scheme was used for momentum convection term that stabilizes the artificial breakup and does not have a detrimental effect on the single-phase turbulence far away from the bubble. All other interpolations and gradients are discretized using linear schemes, which are second-order accurate. The modified solver is able to use any Runge– Kutta scheme. In the present computation, a Diagonally Implicit Runge–Kutta scheme of second order (DIRK2) was used with the CFL number in the simulations below 0.4.

To simulate a Taylor bubble in a counter-current flow under turbulent conditions, a recycling boundary condition was used at the inlet, situated upstream from the Taylor bubble. This recycling process occurs five hydraulic diameters ( D ) from the inlet, allowing sufficient space for the velocity field to develop fully. Beyond the recycling point, a distance of two to three diameters is maintained before the Taylor bubble’s nose, ensuring it doesn’t affect the boundary condition. The flow rate is continuously adjusted at each time step to balance the bubble’s buoyancy against hydrodynamic drag, keeping the bubble’s position relatively stable in the simulation. This method is depicted in Fig. 5 . To counter minor fluctuations, a gentle relaxation factor of 0.01 was employed, ensuring the bubble remains steady.

Schematic of recycling boundary condition inside the computational domain (note the direction of the gravity)

The OpenFOAM model described above was successfully used for simulation of a stagnant Taylor bubble in the counter-current water flow in a thinner pipe at Re = 1400 [ 22 ]. These results were compared with experiments performed under the same conditions. The Re = 1400 case represents laminar flow of water above the bubble, laminar flow in the liquid film and chaotic flow with developing turbulence under the tail of the bubble. The model successfully described the laminar region of the water flow and the turbulent region under the tail of the Taylor bubble. The laminar-turbulent case at Re = 1400, where bubble retains axial symmetry, was a starting point for the present, fully turbulent model at Re = 5600, and the corresponding mesh density.

In the present investigation, characterized by a Reynolds number of 5600, three distinct mesh resolutions were used, all of them prepared with “Salome Meca” tool [ 49 ], with two of them depicted in Fig. 6 . Each mesh shared an identical cylindrical shape, with a length of 0.52 m and a diameter of 26 mm. The G30 mesh consisted of around 700,000 hexahedral cells and the G15 mesh was composed of about 4.1 million cells. The naming convention of the meshes corresponds to the dimensionless spanwise cell size in the bulk flow.

Mesh G15 ( left), G30 (right)

Near the wall regions, the spanwise cell size was maintained at less than one wall unit. This wall unit, denoted as \(d{x}^{+}\) , is defined by the formula \(d{x}^{+} = dxU/\nu\) , where \(dx\) represents the cell width in actual units, \(U\) signifies the friction velocity, and ν is the kinematic viscosity. Along the streamwise direction, the cell sizes were generally kept comparable to those in the spanwise direction, albeit with additional refinement in the vicinity of the bubble.

The OpenFOAM set-up described in this section was used and verified in simulations of Taylor bubble flow in Kren et al. [ 22 ], where laminar liquid flow at Re = 1400 was prescribed at the inlet. The problem considered in [ 22 ] had simpler nature of the flow at the Taylor bubble’s body, but more complex tail behavior than in the present work: Taylor bubble in [ 22 ] was longer and experienced break-up of tiny bubbles at the flapping tail, where laminar to turbulent transition occurred. In the present work, the liquid flow is fully turbulent everywhere, but the bubble is shorter and does not exhibit a significant break-up. The intensity of the bubble breakup was actually the most important parameter that was affected by the mesh density as shown in Fig. 7 ; coarser mesh (G30) bubble has lost larger amount of mass in the same time interval in comparison with the finer mesh (G15). Further comparison of grid sensitivity study shown in Fig. 7 shows different azimuthal orientation of both bubbles, which is randomly established very early in the simulations. Other properties of the Taylor bubble, like the mean mass flow rate and shape of the nose, were rather similar on both meshes. Consequently, only the fine mesh (G15) results are presented in the next sections.

Comparison of instantaneous liquid velocity magnitude fields on G15 (fine—top) and G30 (coarse—bottom) mesh. Bright red denotes air phase. Both drawings are given at the same time t = 10 s in the simulation

The length of the bubble in the OpenFOAM simulation was around 120 mm. Time interval of the simulation was 12 s, which took 110,000 h of CPU time on 192 computer cores.

In this section, we compare one experimental and two simulated bubbles with their main properties collected in Table 3 . One can see that the bubbles are of different length. This was not planned: the initial intention was to have bubbles of the same length in both simulations performed by both groups of researchers. When it was found that bubbles in TrioCFD and OpenFOAM simulations have different lengths, both simulations were running already for a month and a decision was made to continue without changing the length. The decision was based on experimental results described in [ 37 ], which have shown that for the bubbles of the length between two and six diameters, the main properties, like the bubble velocity, shape, and water mass flow rate, do not depend on the length.

As demonstrated in [ 37 ] time-averaged bubble shape is not axisymmetric. Instead the bubble exhibits a quasi-stable asymmetric shape: the bubble is always inclined toward one side of the pipe wall. The azimuthal direction of the inclination is determined during the injection of the bubble. As discussed in [ 37 ], this behavior did not allow predictions of the time-averaged 3D shape of the Taylor bubble in turbulent counter-current flow based on the 2D shadowgraphy measurements. This asymmetry of the bubble can be easily analyzed in 3D simulations, in the 2D photographs however, it is important to perform measurements in the plane, where the bubble asymmetry is maximal. Out of around 10 different experimental cases, where asymmetry was observed at different azimuthal angles, we have selected one with the most pronounced asymmetry in the camera’s field-of-view. Even this case is not exactly perpendicular to the 2D plane of the photograph; however, it is sufficiently close and is chosen as a representative case in the present paper.

The second important parameter for comparison of the Taylor bubbles is the time interval of the observation. Our experience shows that it is ideal to have a time interval of around one minute. As seen in Table 3 , such time intervals were not achievable in simulations due to the high computational costs and/or large numerically induced breakup of the bubble.

When time interval is considered, the influence of the initial conditions in the simulations must be emphasized: both simulations start with symmetric and non-physical shape of the bubble, which is followed by a rather vigorous semi-physical transient. Consequently, a short time interval of a couple of tenths of a second must be neglected in analyses of the results. The second characteristic time in the simulations is the time interval where the initial symmetry of the bubble is broken and a quasi-stable asymmetric bubble shape is obtained. In OpenFOAM simulation the asymmetry was established after 3–5 s. After that time, the comparison of the bubble shape in experiments and simulations is feasible and the total drag of the bubbles can be compared.

As seen in SubSect. 4.1 and in Table 3 , attaining the proper steady-state bubble shape, which is ultimately responsible for the bubble’s drag, was a challenge in OpenFOAM simulation. The ultimate bubble shape predicted by the OpenFOAM had lower drag than the actual experimental bubble. Consequently, 17% higher mass flow rate was needed to keep the bubble stagnant in simulation (Table 3 ).

In the TrioCFD simulation, a fixed mass flow rate (mean water velocity v 0 = 0.18 m/s) and a moving frame of reference were used to keep the bubble in place. Since the TrioCFD simulation did not achieve the steady-state asymmetric shape, the bubble experienced stronger drag force and was moving down with velocity around 0.04 m/s. This motion was compensated with the moving frame of reference. As a rough estimate, the mean downward velocity of water, which would keep the symmetric bubble stagnant, would be around 0.13 m/s. This is about 75% of the measured downward velocity (Table 3 ).

4.1 Taylor Bubble Shape

Typical instantaneous shapes and sizes of the bubbles taken at times several seconds apart are shown in Fig. 8 , while Fig. 9 shows time-averaged bubble shapes. In the OpenFOAM simulation, the interface was defined as an isoline with values of the gas (and liquid) volume fraction equal to 0.5. In TrioCFD this definition is not needed: exact position of the interface markers is available at any time. Time averaging in the experiment was performed over a 2-min interval. In the OpenFOAM simulation, time averaging was performed in the interval from 6 to 12 s, where the bubble lost the symmetry imposed by the initial conditions and developed a roughly steady-state asymmetric shape. In the TrioCFD simulation, the analyzed time interval was only 1 s long and that was not enough for development of the asymmetric shape. Consequently, instantaneous TrioCFD bubble is the same as the time-averaged bubble, only one profile is given in Fig. 8 , and there is no TrioCFD profile in Fig. 9 .

Instantaneous silhouettes of measured Taylor bubble (left), OpenFOAM simulation (center), and TrioCFD simulation (right). Pipe walls are drawn in experimental image. Walls in simulations are left–right edges of the image

Time-averaged Taylor bubble interface position: experiment—2 min time interval (left), OpenFOAM average Taylor bubble position over 6 to 12 s time interval (right)

Time averaging takes into account slow vertical motion of the Taylor bubble in experiment and in simulations. The time-averaged bubble shapes in Fig. 9 are obtained in a moving frame of reference: origin of the coordinate system in axial direction is attached to the axial position of the bubble nose tip at every instantaneous snapshot before averaging.

The time-averaged measured bubble in Fig. 9 is inclined to the right side of the image; however, one of the three instantaneous profiles in Fig. 8 shows a bubble inclined slightly to the left. One can also note that the tail of the bubble is not resolved in all instantaneous experimental cases. The dynamics of the bottom surface is a strong 3D phenomenon, and capturing the tail position from 2D shadowgraphy does not give a particularly useful information. Consequently, the software for interface identification was not forced to work in this region.

Three instantaneous shapes of the bubble from OpenFOAM simulation are given in five seconds intervals in Fig. 8 , center: the first silhouette shown 1 s after the start of simulation is showing nearly symmetric bubble, which has not achieved the quasi-steady asymmetric shape yet. Symmetry is broken and developed at times 6 s and 11 s. These two silhouettes exhibit higher asymmetry than their experimental counterparts. Consequently, such a shape of the bubble exhibits lower drag and requires a higher mass flow rate for dynamical balance, as reflected in Table 3 .

As seen from the experimental silhouettes in Fig. 8 the bubble’s nose occasionally crosses the axis; however, on average, it remains attached to the same azimuthal angle of the pipe throughout the several minute time interval. This phenomenon is further demonstrated in Fig. 10 : 12 s time interval allows direct comparison with the OpenFOAM simulation. Wobbling of the nose is stronger in the experiment and less intensive in the OpenFOAM simulation. The important information from Fig. 10 is more intensive fluctuations of the experimental bubble in comparison with the simulated bubble from OpenFOAM simulation. This is a clear sign that the existing OpenFOAM model cannot provide a perfect description of the phenomena.

Radial position of Taylor bubble’s nose

Transition from symmetric OpenFOAM bubble to quasi-stable asymmetric one is also rather clearly seen in Fig. 10 . The simulations started with an axially symmetric Taylor bubble, and the bubble nose position has moved to the wall in about three to five seconds. After that the bubble nose stays close to the wall and the final asymmetry of OpenFOAM bubble is much more pronounced than in the measurements.

Deviations from the experiment are not without consequences: next to the higher liquid mass flow rate needed to counter-balance the OpenFOAM bubble given in Table 3 , simulated bubble creates a very thin liquid film seen on the right side of the 2D image in Fig. 9 (center). The film eventually becomes so thin that it ruptures and the air comes into the direct contact with the pipe wall. This phenomenon does not have a physical background since it was never observed in experiments. Consequently, the simulations are stopped at such instances and subgrid models of interface friction and surface tension are being investigated to improve that behavior.

The asymmetry in the bubble of the TrioCFD simulation was not achieved in the observed time interval, thus its long-time behavior cannot be predicted at this point. Nonetheless, during that time frame, radial motion of the bubble nose was observed, but it was not relevant to compare as it was only about one percent of the pipe diameter. The axial velocity of the TrioCFD bubble was 0.04 m/s downward and this was taken into account in Table 3 mass flow rate ratio calculation. This seemingly larger difference is due to the higher drag coefficient of the symmetric bubble compared to the asymmetric one. This ratio cannot be used to extrapolate the final mass flow rate that would balance the TrioCFD bubble once the quasi-stable asymmetric shape is reached.

4.2 Liquid Film Thickness and Interface Axial Velocity

The asymmetry observed in the time-averaged Taylor bubble, as depicted in Sect. 4.1 , presents challenges when it comes to independently verifying our measurements. However, a way to mitigate this issue was averaging the bubble shape and corresponding liquid film thickness over both sides of the photographs. These findings are presented in Fig. 11 , which illustrates the liquid film thickness along the bubble. The axial distances along the z -axis of Fig. 11 are measured from the bubble nose. Solid lines represent the time-averaged and left–right spatial averaged profile derived from the measurements and simulations. Dashed lines represent time-averaged left and right (thick and thin film) profiles separately, i.e., magnification of the near-wall region in Fig. 9 . The magnification of the film thickness in Fig. 11 shows that the average thickness is very similar in experiment and OpenFOAM simulation. Figure 11 is clearly exposing the feature mentioned above: bubble asymmetry is more pronounced in OpenFOAM simulation than in the experiment and the difference between the thick and thin film side is larger in OpenFOAM simulation.

Average liquid film thickness: solid lines. Dashed lines: thick and thin films. Measurement uncertainty is below 0.1 mm and is not plotted

The approximately 25% thinner film in TrioCFD simulation is due to the lower drag of the symmetric bubble, which is proportional to the reduced effective mass flow rate (effective mass flow rate is equal to imposed mass flow rate minus moving frame of reference contribution). Since the thick and thin films in TrioCFD are equal to the average, only one profile is shown in Fig. 11 .

By utilizing the averaged film thickness profiles from the measurements, an additional curve related to the mean downward liquid velocity in the film region can be derived. Based on the continuity equation and known upstream liquid velocity v 0 (0.179 m/s), the mean liquid velocity can be calculated as \(v(z)={v}_{0}{R}^{2}/[2Rh\left(z\right)-{h(z)}^{2}]\) , where R represents the pipe radius (13 mm) and h(z) represents the liquid film thickness at a given axial position z . By assuming the measured film thickness, one can calculate the mean liquid velocity within the film region. However, the quantity of interest is interface velocity and with the presented measurement techniques it cannot be measured. Nevertheless, a reasonably good approximation is available: the velocity of the interface can be estimated from the mean liquid velocity based on the liquid film thickness. The interface velocity was obtained from the mean liquid film velocity by multiplication with a factor of 1.15. This semi-empirical factor stems from the DNS simulations of the turbulent flume [ 50 ] and contains relative error around 2–3% [ 37 ]. It applies to the fully developed free liquid surface near an infinite flat wall and disregards the air shear force. As shown in [ 37 ], this approximation can be used, because the interface velocity is very similar on all sides of the bubble and does not depend on the thickness of the liquid film.

In simulations, the interface velocity can be obtained directly from the data. In the OpenFOAM results, the interface velocity is defined as a velocity at the isoline with the values of the gas (and liquid) volume fraction equal to 0.5. In the TrioCFD results, this velocity is directly obtained as a velocity of the Lagrangian marker points on the interface.

Figure 12 presents the experimental interface velocity profile for the time-averaged and spatially left–right averaged film and interface velocities from simulations. The relative uncertainty of the measured time-averaged velocity profile is similar in magnitude to the uncertainty of the mean film thickness measurement, approximately 10% at distances greater one diameter D from the bubble nose.

Taylor bubble interface velocity (m/s): OpenFOAM and TrioCFD—obtained directly from simulations. Experiment—obtained from film thickness and continuity equation. OpenFOAM: left and right interface velocity

Numerical interface velocity profiles in Fig. 12 can be easily extracted for each side of the Taylor bubble separately and are also plotted separately for OpenFOAM simulation. Only one profile is given for TrioCFD simulation in Fig. 12 due to the symmetry of the bubble.

As further explained in [ 37 ] and in Sect. 4.3 , where interface velocity is analyzed with a different approach, very similar interface velocities are expected on both sides of the Taylor bubble. Nevertheless, the OpenFOAM simulation shows very good agreement of the interface velocity only on the thick side of the liquid film. Significantly slower interface velocity is observed in the region of the thin film. Mesh resolution in OpenFOAM G15 mesh simulation describes 0.5 mm liquid film with around 10 mesh points in radial direction. This is actually coarse for an accurate description of a turbulent film with LES. If we add that the interface is smeared over 2 to 3 points, we can conclude that the higher radial resolution or a more elaborated subgrid model is needed around such interface.

The velocity profile of the TrioCFD simulation is close to the measurements and within the uncertainty of the measurements, which are characterized with a single uncertainty bar at around z = 70 mm. It is clear that the markers are accurate in specifying the location and the velocity of the interface. Nevertheless, the high similarity between the TrioCFD and measured interface velocities is due to the fact that the walls in the TrioCFD simulation are moving up at around 0.04 m/s along with the moving frame of reference, while the bubble is fixed in space.

4.3 Axial Velocities of Disturbance Waves on the Interface

The presented measurement techniques and image processing algorithms allow us to track small disturbance waves traveling along the Taylor bubble interface [ 43 , 44 ]. This technique was used and described by Kren et al. [ 37 ]. The specific mechanisms generating these waves are not entirely clear, but the waves are believed to be induced by the turbulence. However, assuming that most of the waves are produced by random disturbances, they are expected to travel in all directions parallel to the air–water interface. The velocities of these waves are governed by the capillary wave equations, as described in [ 5 ]. The dispersion relation of capillary waves can be expressed as:

\(\omega^{2} = \frac{{{ }\sigma k^{3} }}{\rho }{\text{tanh}}\left( {k d} \right)\) ,

where \(k=2\pi /\lambda\) is the wavenumber, \(\omega =\) \(2\pi \nu\) angular frequency, and \(c=\) \(\lambda \nu\) is the phase velocity. For typical “thick” 2 mm liquid film waves, the characteristic frequencies, wavelengths, and phase velocities are approximately 1 Hz, 50 mm, and 0.05 m/s, respectively. For the thinner 0.5 mm liquid film, these values are approximately 40 Hz, 5 mm, and 0.2 m/s. These estimates indicate that the characteristic phase velocities of the waves are lower than the interface velocities shown in Fig. 12 , implying that practically all waves on the interface travel downward.

To estimate the axial velocities of the disturbance waves traveling over the interface, measurements of the axial disturbance wave velocity w are performed using cross-correlations of the time signals at various axial positions along the pipe. By selecting a distance H between specific points in space, for example, H = 200 pixels, the velocity w can be obtained from the measured time lag τ of the signals as w = H/τ . For example, the time lag at the point 400 pixels downstream of the bubble nose and at a distance H = 200 pixels, is computed from the cross-correlation of time signals at points 400 − H /2 = 300 pixels and 400 + H /2 = 500 pixels. The procedure is described in [ 37 ], where it was applied to the measurements.

The same procedure was used also for analyses of the disturbance wave velocities in the OpenFOAM simulation results and the results are presented in Fig. 13 together with the interface velocities. Velocities are given for one real and two simulated Taylor bubbles listed in Table 3 . The disturbance wave speed profiles are derived from the time lags observed in the right-hand side of the silhouettes, except for TrioCFD results, where both sides are symmetric and the results are very similar and not repeated twice.

Disturbance velocity (dashed) vs. interface velocity (solid) in the experiment (top-left), TrioCFD (top-right), and OpenFOAM (bottom-left [0.3 s:3.6 s] interval and bottom-right [8.4 s:11.8 s] interval)

The complete time history consisting of 50,000 frames over 125 s interval is analyzed for measurement. In the OpenFOAM results two intervals of the same length 3.4 s at the beginning and at the end of simulation (50–2050 frames and 5000–7000 out of total 7000 frames) were used. In the TrioCFD simulation around 1700 frames were analyzed over a 1.7 s interval. Cross-correlations are compared at a fixed distance of around 11 mm in measurements and in OpenFOAM, and 20 mm in TrioCFD. The discrete values of cross-correlation time lags are smoothed using parabolic interpolation.

Figure 13 shows disturbance velocities and the corresponding interface velocities in experiment and in simulations. They are separated into four separated graphs plotted on the same spatial scale and with the same velocity range in order to make the differences and similarities clear. Both distinct types of velocity profiles are obtained from the same measurements but through entirely different analysis. The interface velocities are obtained directly from the simulations and from the measurement of the liquid film thickness in the experiment. On the other hand, the disturbance velocities are determined based on the relative motions of the liquid–air interface. Notably, both types of velocities exhibit remarkable similarity in most of the graphs in Fig. 13 . This observation confirms the hypothesis given in [ 37 ] that the time-averaged velocity of the disturbance waves on the water–air interface effectively represents the velocity of the interface itself.

Before proceeding to the further discussion it is important to address the discrepancies seen in the graphs of Fig. 13 . Disturbance velocity profiles obtained in experiment show very similar disturbance wave velocities on both sides of the photograph, despite significant difference in the liquid film thickness seen in Fig. 8 and in Fig. 11 . Similar observation was reported in other experimental cases in [ 37 ]. Further observation of experimental profiles shows increasing discrepancies on the right side of the photographs in the region beyond 70 mm from the bubble’s nose. This discrepancy appears in the region of poorer spatial resolution in the thin film, which is resolved on 2–5 pixels. Very thin liquid film filters the long wavelengths, which are the most relevant for accurate evaluation of the disturbance velocity measurements. Short wavelengths, which remain on the thin films, are more difficult to resolve with the limited resolution of the presented experiment. The only solution is to increase the spatial resolution of the photographs.

The disturbance velocities in TrioCFD were obtained in 8 points along the bubble, which are marked with symbols in Fig. 13 . Computation of cross-correlation functions is difficult and sensitive to the noise even on the fixed meshes of the photographs and OpenFOAM results. The problem becomes even more difficult for TrioCFD, where cross-correlation functions must be obtained from the moving markers on the interface. Consequently, for the given spatial resolution, only very rough estimates of disturbance velocities are available in TrioCFD (Fig. 13 ).

Lastly, we need to comment on the disturbance wave velocities computed from the OpenFOAM results using the same procedure as in the experiment. Two separate graphs are shown in Fig. 13 for OpenFOAM, one for the interval at the beginning of the simulation during the time interval [0.3 s: 3.6 s] where the bubble is losing its symmetry, and the other for the time interval [8.4 s: 11.9 s] where the bubble is close to quasi-steady-state and with a very thin liquid film on the left side plane shown in Fig. 8 . Disturbance velocity profiles computed in the first time interval where the Taylor bubble is close symmetric are not smooth, but reasonably close to the computed interface velocities. Coarse, ~ 0.05 mm, radial resolution in the near wall region can only provide a very rough approximations of the disturbances with amplitudes 0.01–0.05 mm.

The problem is more exaggerated in the time interval at the end of the OpenFOAM simulation. At that time, the liquid film becomes very thin on one side and rather thick on the other side. As shown in Fig. 13 the cross-correlation technique still works for the thin film (not with a great precision), but fails on the thick side. The reason for this failure is film position, which is not within the finely resolved boundary layer visible in G15 mesh of Fig. 6 , but in the coarser central region where small disturbance waves cannot be captured anymore.

The equivalence between the time-averaged velocities of the interface waves and the convective velocity of the interface observed in experiments, is thus roughly confirmed also in simulations. The main reason for the equivalence lies in the fact that the characteristic velocities of the dominant disturbance waves are significantly lower, at least by an order of magnitude, compared to the mean velocities of the liquid film (approximately 1 m/s). As a result, the time averaging process predicts the final disturbance wave velocity equal to the time-averaged convective velocity of the water–air interface.

The final comparison of the experiment and simulations is focused on spectra of the disturbance waves traveling in the axial direction over the body of the Taylor bubble. Figure 14 shows power spectra of the disturbance waves analyzed in a point approximately 50 mm below the Taylor bubble’s nose. The common property of measured and TrioCFD spectra is very sharp drop at frequencies above 10–20 Hz. An exception is seen in the OpenFOAM results and we assume that the difference is due to the implemented numerical scheme in combination with the LES-WALE mode, which does not sufficiently suppress the fluctuations in the range of frequencies between 10 and 70 Hz.

Power spectra of interface disturbance waves at point 50 mm downstream the bubble’s nose

The highest frequencies of the turbulent fluctuations in the single-phase flow of water above the bubble can be estimated from the DNS database of Kasagi (Fukata and Kasagi, 2002) pipe flow case at Re = 5300, which is close to the present experimental conditions. Their highest frequencies of Kolmogorov scale vortices are between 10 and 70 Hz in the axis of the pipe and in the near-wall region, respectively. Since the turbulent kinetic energy in the vortices at the Kolmogorov scales is low, frequencies between 3 and 20 Hz, which correspond to the Taylor microscales, seem to be more relevant as the upper limits.

Spectral analysis of the waves traveling over the Taylor bubble’s body shown in Fig. 14 is representative also at other distances from the bubble’s nose.

5 Conclusions

This paper summarizes the studies of the Taylor bubble in a vertical turbulent counter-current air–water flow, excluding the bubble’s tail region. The analyses are based on results available from high-precision 2D shadowgraphy observations which are compared with high-fidelity simulations with two different computer codes and numerical schemes: OpenFOAM is using geometrical VOF interface tracking, while the TrioCFD code is based on explicit front tracking method. Considered Taylor bubble was observed in the inertia dominant regime, where the influence of viscosity and surface tension are minor.

The primary goal of this study was to compare the time-averaged shape of the Taylor bubble’s interface. From the comparison between the experimental data and the OpenFOAM simulation—which used a model verified and validated on the case of a stagnant Taylor bubble in a laminar counter-current flow [ 22 ] —two main findings emerged:

The bubble asymmetry in the simulation was more pronounced than that observed in the experiments, resulting in lower bubble drag and, consequently, a roughly 20% higher liquid mass flow rate needed to keep the bubble stationary.

A less critical, but still relevant issue: fluctuations around the time-averaged bubble shape were weaker in the simulation than in the experiment.

The simulation of TrioCFD was performed with a more expensive numerical approach and only one second of transient was analyzed. This was not enough to develop an asymmetric bubble shape. Consequently, only qualitative bubble shape comparison was performed.

The second part of the study was focused on dynamics of interfacial waves traveling over the body of the Taylor bubble. Our analyses of various experiments in [ 37 ] have shown that the disturbance wave velocity, measured over a sufficiently long interval of several tens of seconds, becomes equal to the axial water–air interface velocity. The cross-correlation measurements primarily capture low-frequency waves, which are slower than the interface velocity. Therefore, tracking these waves provides a technique for measuring the time-averaged interface velocity.

The same analysis of disturbance waves on the interface was performed in both numerical simulations, where the accuracy of the analyses was severely limited with the spatial discretization of both simulations. Refined mesh in the near-wall region was barely sufficient to capture the disturbance waves and to reconstruct their propagation velocities in OpenFOAM. The specific numerical approach of TrioCFD was even less appropriate for disturbance velocity measurements and allowed only rough approximation. When the interface fell out of the refined mesh in the near-wall region into the coarse meshing in the center of the pipe in OpenFOAM simulation, disturbance waves were not recognized anymore.

Spectra of the interfacial waves were compared at a point fixed from the bubble’s nose. TrioCFD showed greater precision than OpenFOAM, accurately reflecting the sharp frequency decline above 10–20 Hz observed in experiments. In contrast, OpenFOAM’s spectra erroneously displayed significant frequencies up to 70 Hz, likely misrepresenting the physical phenomena.

The stagnant Taylor bubble in turbulent low-Reynolds counter-current flow was identified as a challenging test case for two advanced interface tracking models in the TrioCFD and OpenFOAM codes, even though they were both well validated in laminar conditions [ 22 , 41 ]. We demonstrated that fine spatial resolution is necessary not only in the near-wall region, where the liquid boundary layer forms, but also at the interface itself. Future simulations with both codes will aim to enhance the subgrid models for interface friction and surface tension.

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Acknowledgements

The authors gratefully acknowledge financial support provided by Slovenian Research Agency, grant P2-0026 and Slovenia-CEA grant NC-0026. The TrioCFD computations were made possible by the granted access to the HPC resources of IDRIS under the allocation 2023-R0131010339 made by GENCI.

Funding was provided by Javna Agencija za Raziskovalno Dejavnost RS, NC-0026, Iztok Tiselj, P2-0026

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Jožef Stefan Institute, Jamova 39, 1000, Ljubljana, Slovenia

Iztok Tiselj, Jan Kren & Blaž Mikuž

Faculty of Mathematics and Physics, University of Ljubljana, Jadranska Ulica 19, 1000, Ljubljana, Slovenia

Iztok Tiselj & Jan Kren

Service de Thermohydraulique Et de Mécanique Des Fluides, Université Paris-Saclay, CEA, 91191, Gif-Sur-Yvette, France

Raksmy Nop, Alan Burlot & Grégoire Hamrit

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Correspondence to Iztok Tiselj .

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Tiselj, I., Kren, J., Mikuž, B. et al. Experimental and Numerical Study of Taylor Bubble in Counter-Current Turbulent Flow. Arab J Sci Eng (2024). https://doi.org/10.1007/s13369-024-09489-2

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Received : 11 March 2024

Accepted : 28 July 2024

Published : 21 August 2024

DOI : https://doi.org/10.1007/s13369-024-09489-2

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Quasi-Experimental Design | Definition, Types & Examples

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Example of a true experiment vs a quasi-experiment

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Nonequivalent groups design

Regression discontinuity

Natural experiments

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Quasi Experimental Design Overview & Examples

What is a Quasi Experimental Design?

When to Use Quasi-Experimental Design

Types of Quasi-Experimental Designs and Examples

Natural Experiments

Nonequivalent Groups Design

Regression Discontinuity

Controlling Confounders in a Quasi-Experimental Design

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Quasi-Experimental Research Design – Types, Methods

Quasi-Experimental Design

Types of Quasi-Experimental Design

Non-Equivalent Control Group Design

Interrupted Time-Series Design

Pretest-Posttest Design

Regression Discontinuity Design

Natural Experiments

Data Analysis Methods

Descriptive Statistics

Inferential Statistics

Propensity Score Matching

Difference-in-differences Analysis

Interrupted Time Series Analysis

Regression Discontinuity Analysis

Steps in Quasi-Experimental Design

Quasi-Experimental Design Examples

Applications of Quasi-Experimental Design

When to use Quasi-Experimental Design

Purpose of Quasi-Experimental Design

Advantages of Quasi-Experimental Design

Limitations of Quasi-Experimental Design

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Muhammad Hassan

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7.3 Quasi-Experimental Research

Nonequivalent Groups Design

Pretest-Posttest Design

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Key Takeaways

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A Modern Guide to Understanding and Conducting Research in Psychology

7.1 Nonequivalent Groups Design

7.2 Pretest-Posttest Design

7.3 Interrupted Time Series Design

7.4 Combination Designs

KEY TAKEAWAYS

regression to the mean

Overview of Single-Subject Research

The Case of “Anna O.”

Assumptions of Single-Subject Research

Who Uses Single-Subject Research?

Single-Subject Research Designs

Reversal Designs

Multiple-Baseline Designs

Data Analysis in Single-Subject Research