single study research design

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Single-Subject Research

45 Single-Subject Research Designs

Learning objectives.

• Describe the basic elements of a single-subject research design.
• 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.

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 10.1, 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 10.1 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.)

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) [1] . 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. There may be a period of adjustment to the treatment during which the behavior of interest becomes more variable and begins to increase or decrease. 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 employed an ABAB reversal design. Figure 10.2 approximates the data for Robbie. 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? Why use an ABA design, for example, rather than a simpler AB design? Notice that an AB design is essentially an interrupted time-series design applied to an individual participant. Recall that one problem with that design is that 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 (assuming that the treatment does not create a permanent effect), 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.

There are close relatives of the basic reversal design that allow for the evaluation of more than one treatment. In a  multiple-treatment reversal design , a baseline phase is followed by separate phases in which different treatments are introduced. For example, a researcher might establish a baseline of studying behavior for a disruptive student (A), then introduce a treatment involving positive attention from the teacher (B), and then switch to a treatment involving mild punishment for not studying (C). The participant could then be returned to a baseline phase before reintroducing each treatment—perhaps in the reverse order as a way of controlling for carryover effects. This particular multiple-treatment reversal design could also be referred to as an ABCACB design.

In an  alternating treatments design , two or more treatments are alternated relatively quickly on a regular schedule. For example, positive attention for studying could be used one day and mild punishment for not studying the next, and so on. Or one treatment could be implemented in the morning and another in the afternoon. The alternating treatments design can be a quick and effective way of comparing treatments, but only when the treatments are fast acting.

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 child with an intellectual delay, 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. Perhaps something else happened at about the same time as the treatment—for example, the student’s parents might have started rewarding him for good grades. One solution to these problems is to use a  multiple-baseline design , which is represented in Figure 10.3. There are three different types of multiple-baseline designs which we will now consider.

Multiple-Baseline Design Across Participants

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 unlikely to be a coincidence.

As an example, consider a study by Scott Ross and Robert Horner (Ross & Horner, 2009) [2] . 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. 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 the student’s 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—a very unlikely occurrence—to explain their results.

Multiple-Baseline Design Across Behaviors

In another version of the multiple-baseline design, multiple baselines are established for the same participant but for different dependent variables, and the treatment is introduced at a different time for each dependent variable. Imagine, for example, a study on the effect of setting clear goals on the productivity of an office worker who has two primary tasks: making sales calls and writing reports. Baselines for both tasks could be established. For example, the researcher could measure the number of sales calls made and reports written by the worker each week for several weeks. Then the goal-setting treatment could be introduced for one of these tasks, and at a later time the same treatment could be introduced for the other task. The logic is the same as before. If productivity increases on one task after the treatment is introduced, it is unclear whether the treatment caused the increase. But if productivity increases on both tasks after the treatment is introduced—especially when the treatment is introduced at two different times—then it seems much clearer that the treatment was responsible.

Multiple-Baseline Design Across Settings

In yet a third version of the multiple-baseline design, multiple baselines are established for the same participant but in different settings. For example, a baseline might be established for the amount of time a child spends reading during his free time at school and during his free time at home. Then a treatment such as positive attention might be introduced first at school and later at home. Again, if the dependent variable changes after the treatment is introduced in each setting, then this gives the researcher confidence that the treatment is, in fact, responsible for the change.

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. Group data are described using statistics such as means, standard deviations, correlation coefficients, and so on to detect general patterns. Finally, 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 10.4, 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 10.4, 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.

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) [3] . (Note that averaging  across  participants is less common.) Another approach is to compute the  percentage of non-overlapping data  (PND) for each participant (Scruggs & Mastropieri, 2001) [4] . 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 non-overlapping 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.

Image Description

Figure 10.2 long description:  Line graph showing the results of a study with an ABAB reversal design. The dependent variable was low during first baseline phase; increased during the first treatment; decreased during the second baseline, but was still higher than during the first baseline; and was highest during the second treatment phase.  [Return to Figure 10.2]

Figure 10.3 long description:  Three line graphs showing the results of a generic multiple-baseline study, in which different baselines are established and treatment is introduced to participants at different times.

For Baseline 1, treatment is introduced one-quarter of the way into the study. The dependent variable ranges between 12 and 16 units during the baseline, but drops down to 10 units with treatment and mostly decreases until the end of the study, ranging between 4 and 10 units.

For Baseline 2, treatment is introduced halfway through the study. The dependent variable ranges between 10 and 15 units during the baseline, then has a sharp decrease to 7 units when treatment is introduced. However, the dependent variable increases to 12 units soon after the drop and ranges between 8 and 10 units until the end of the study.

For Baseline 3, treatment is introduced three-quarters of the way into the study. The dependent variable ranges between 12 and 16 units for the most part during the baseline, with one drop down to 10 units. When treatment is introduced, the dependent variable drops down to 10 units and then ranges between 8 and 9 units until the end of the study.  [Return to Figure 10.3]

Figure 10.4 long description:  Two graphs showing the results of a generic single-subject study with an ABA design. In the first graph, under condition A, level is high and the trend is increasing. Under condition B, level is much lower than under condition A and the trend is decreasing. Under condition A again, level is about as high as the first time and the trend is increasing. For each change, latency is short, suggesting that the treatment is the reason for the change.

In the second graph, under condition A, level is relatively low and the trend is increasing. Under condition B, level is a little higher than during condition A and the trend is increasing slightly. Under condition A again, level is a little lower than during condition B and the trend is decreasing slightly. It is difficult to determine the latency of these changes, since each change is rather minute, which suggests that the treatment is ineffective.  [Return to Figure 10.4]

• Sidman, M. (1960). Tactics of scientific research: Evaluating experimental data in psychology . Boston, MA: Authors Cooperative. ↵
• Ross, S. W., & Horner, R. H. (2009). Bully prevention in positive behavior support. Journal of Applied Behavior Analysis, 42 , 747–759. ↵
• Fisch, G. S. (2001). Evaluating data from behavioral analysis: Visual inspection or statistical models. Behavioral Processes, 54 , 137–154. ↵
• Scruggs, T. E., & Mastropieri, M. A. (2001). How to summarize single-participant research: Ideas and applications.  Exceptionality, 9 , 227–244. ↵

When the researcher waits until the participant’s behavior in one condition becomes fairly consistent from observation to observation before changing conditions.

The most basic single-subject research design in which the researcher measures the dependent variable in three phases: Baseline, before a treatment is introduced (A); after the treatment is introduced (B); and then a return to baseline after removing the treatment (A). It is often called an ABA design.

Another term for reversal design.

The beginning phase of an ABA design which acts as a kind of control condition in which the level of responding before any treatment is introduced.

In this design the baseline phase is followed by separate phases in which different treatments are introduced.

In this design two or more treatments are alternated relatively quickly on a regular schedule.

In this design, multiple baselines are either established for one participant or one baseline is established for many participants.

This means plotting individual participants’ data, looking carefully at those plots, and making judgments about whether and to what extent the independent variable had an effect on the dependent variable.

This is the percentage of responses in the treatment condition that are more extreme than the most extreme response in a relevant control condition.

Research Methods in Psychology Copyright © 2019 by Rajiv S. Jhangiani, I-Chant A. Chiang, Carrie Cuttler, & Dana C. Leighton is licensed under a Creative Commons Attribution-NonCommercial-ShareAlike 4.0 International License , except where otherwise noted.

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Research Design 101

Everything You Need To Get Started (With Examples)

By: Derek Jansen (MBA) | Reviewers: Eunice Rautenbach (DTech) & Kerryn Warren (PhD) | April 2023

Navigating the world of research can be daunting, especially if you’re a first-time researcher. One concept you’re bound to run into fairly early in your research journey is that of “ research design ”. Here, we’ll guide you through the basics using practical examples , so that you can approach your research with confidence.

Overview: Research Design 101

What is research design.

• Research design types for quantitative studies
• Video explainer : quantitative research design
• Research design types for qualitative studies
• Video explainer : qualitative research design
• How to choose a research design
• Key takeaways

Research design refers to the overall plan, structure or strategy that guides a research project , from its conception to the final data analysis. A good research design serves as the blueprint for how you, as the researcher, will collect and analyse data while ensuring consistency, reliability and validity throughout your study.

Understanding different types of research designs is essential as helps ensure that your approach is suitable  given your research aims, objectives and questions , as well as the resources you have available to you. Without a clear big-picture view of how you’ll design your research, you run the risk of potentially making misaligned choices in terms of your methodology – especially your sampling , data collection and data analysis decisions.

The problem with defining research design…

One of the reasons students struggle with a clear definition of research design is because the term is used very loosely across the internet, and even within academia.

Some sources claim that the three research design types are qualitative, quantitative and mixed methods , which isn’t quite accurate (these just refer to the type of data that you’ll collect and analyse). Other sources state that research design refers to the sum of all your design choices, suggesting it’s more like a research methodology . Others run off on other less common tangents. No wonder there’s confusion!

In this article, we’ll clear up the confusion. We’ll explain the most common research design types for both qualitative and quantitative research projects, whether that is for a full dissertation or thesis, or a smaller research paper or article.

Research Design: Quantitative Studies

Quantitative research involves collecting and analysing data in a numerical form. Broadly speaking, there are four types of quantitative research designs: descriptive , correlational , experimental , and quasi-experimental . 

Descriptive Research Design

As the name suggests, descriptive research design focuses on describing existing conditions, behaviours, or characteristics by systematically gathering information without manipulating any variables. In other words, there is no intervention on the researcher’s part – only data collection.

For example, if you’re studying smartphone addiction among adolescents in your community, you could deploy a survey to a sample of teens asking them to rate their agreement with certain statements that relate to smartphone addiction. The collected data would then provide insight regarding how widespread the issue may be – in other words, it would describe the situation.

The key defining attribute of this type of research design is that it purely describes the situation . In other words, descriptive research design does not explore potential relationships between different variables or the causes that may underlie those relationships. Therefore, descriptive research is useful for generating insight into a research problem by describing its characteristics . By doing so, it can provide valuable insights and is often used as a precursor to other research design types.

Correlational Research Design

Correlational design is a popular choice for researchers aiming to identify and measure the relationship between two or more variables without manipulating them . In other words, this type of research design is useful when you want to know whether a change in one thing tends to be accompanied by a change in another thing.

For example, if you wanted to explore the relationship between exercise frequency and overall health, you could use a correlational design to help you achieve this. In this case, you might gather data on participants’ exercise habits, as well as records of their health indicators like blood pressure, heart rate, or body mass index. Thereafter, you’d use a statistical test to assess whether there’s a relationship between the two variables (exercise frequency and health).

As you can see, correlational research design is useful when you want to explore potential relationships between variables that cannot be manipulated or controlled for ethical, practical, or logistical reasons. It is particularly helpful in terms of developing predictions , and given that it doesn’t involve the manipulation of variables, it can be implemented at a large scale more easily than experimental designs (which will look at next).

That said, it’s important to keep in mind that correlational research design has limitations – most notably that it cannot be used to establish causality . In other words, correlation does not equal causation . To establish causality, you’ll need to move into the realm of experimental design, coming up next…

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Experimental Research Design

Experimental research design is used to determine if there is a causal relationship between two or more variables . With this type of research design, you, as the researcher, manipulate one variable (the independent variable) while controlling others (dependent variables). Doing so allows you to observe the effect of the former on the latter and draw conclusions about potential causality.

For example, if you wanted to measure if/how different types of fertiliser affect plant growth, you could set up several groups of plants, with each group receiving a different type of fertiliser, as well as one with no fertiliser at all. You could then measure how much each plant group grew (on average) over time and compare the results from the different groups to see which fertiliser was most effective.

Overall, experimental research design provides researchers with a powerful way to identify and measure causal relationships (and the direction of causality) between variables. However, developing a rigorous experimental design can be challenging as it’s not always easy to control all the variables in a study. This often results in smaller sample sizes , which can reduce the statistical power and generalisability of the results.

Moreover, experimental research design requires random assignment . This means that the researcher needs to assign participants to different groups or conditions in a way that each participant has an equal chance of being assigned to any group (note that this is not the same as random sampling ). Doing so helps reduce the potential for bias and confounding variables . This need for random assignment can lead to ethics-related issues . For example, withholding a potentially beneficial medical treatment from a control group may be considered unethical in certain situations.

Quasi-Experimental Research Design

Quasi-experimental research design is used when the research aims involve identifying causal relations , but one cannot (or doesn’t want to) randomly assign participants to different groups (for practical or ethical reasons). Instead, with a quasi-experimental research design, the researcher relies on existing groups or pre-existing conditions to form groups for comparison.

For example, if you were studying the effects of a new teaching method on student achievement in a particular school district, you may be unable to randomly assign students to either group and instead have to choose classes or schools that already use different teaching methods. This way, you still achieve separate groups, without having to assign participants to specific groups yourself.

Naturally, quasi-experimental research designs have limitations when compared to experimental designs. Given that participant assignment is not random, it’s more difficult to confidently establish causality between variables, and, as a researcher, you have less control over other variables that may impact findings.

All that said, quasi-experimental designs can still be valuable in research contexts where random assignment is not possible and can often be undertaken on a much larger scale than experimental research, thus increasing the statistical power of the results. What’s important is that you, as the researcher, understand the limitations of the design and conduct your quasi-experiment as rigorously as possible, paying careful attention to any potential confounding variables .

Research Design: Qualitative Studies

There are many different research design types when it comes to qualitative studies, but here we’ll narrow our focus to explore the “Big 4”. Specifically, we’ll look at phenomenological design, grounded theory design, ethnographic design, and case study design.

Phenomenological Research Design

Phenomenological design involves exploring the meaning of lived experiences and how they are perceived by individuals. This type of research design seeks to understand people’s perspectives , emotions, and behaviours in specific situations. Here, the aim for researchers is to uncover the essence of human experience without making any assumptions or imposing preconceived ideas on their subjects.

For example, you could adopt a phenomenological design to study why cancer survivors have such varied perceptions of their lives after overcoming their disease. This could be achieved by interviewing survivors and then analysing the data using a qualitative analysis method such as thematic analysis to identify commonalities and differences.

Phenomenological research design typically involves in-depth interviews or open-ended questionnaires to collect rich, detailed data about participants’ subjective experiences. This richness is one of the key strengths of phenomenological research design but, naturally, it also has limitations. These include potential biases in data collection and interpretation and the lack of generalisability of findings to broader populations.

Grounded Theory Research Design

Grounded theory (also referred to as “GT”) aims to develop theories by continuously and iteratively analysing and comparing data collected from a relatively large number of participants in a study. It takes an inductive (bottom-up) approach, with a focus on letting the data “speak for itself”, without being influenced by preexisting theories or the researcher’s preconceptions.

As an example, let’s assume your research aims involved understanding how people cope with chronic pain from a specific medical condition, with a view to developing a theory around this. In this case, grounded theory design would allow you to explore this concept thoroughly without preconceptions about what coping mechanisms might exist. You may find that some patients prefer cognitive-behavioural therapy (CBT) while others prefer to rely on herbal remedies. Based on multiple, iterative rounds of analysis, you could then develop a theory in this regard, derived directly from the data (as opposed to other preexisting theories and models).

Grounded theory typically involves collecting data through interviews or observations and then analysing it to identify patterns and themes that emerge from the data. These emerging ideas are then validated by collecting more data until a saturation point is reached (i.e., no new information can be squeezed from the data). From that base, a theory can then be developed .

As you can see, grounded theory is ideally suited to studies where the research aims involve theory generation , especially in under-researched areas. Keep in mind though that this type of research design can be quite time-intensive , given the need for multiple rounds of data collection and analysis.

Ethnographic Research Design

Ethnographic design involves observing and studying a culture-sharing group of people in their natural setting to gain insight into their behaviours, beliefs, and values. The focus here is on observing participants in their natural environment (as opposed to a controlled environment). This typically involves the researcher spending an extended period of time with the participants in their environment, carefully observing and taking field notes .

All of this is not to say that ethnographic research design relies purely on observation. On the contrary, this design typically also involves in-depth interviews to explore participants’ views, beliefs, etc. However, unobtrusive observation is a core component of the ethnographic approach.

As an example, an ethnographer may study how different communities celebrate traditional festivals or how individuals from different generations interact with technology differently. This may involve a lengthy period of observation, combined with in-depth interviews to further explore specific areas of interest that emerge as a result of the observations that the researcher has made.

As you can probably imagine, ethnographic research design has the ability to provide rich, contextually embedded insights into the socio-cultural dynamics of human behaviour within a natural, uncontrived setting. Naturally, however, it does come with its own set of challenges, including researcher bias (since the researcher can become quite immersed in the group), participant confidentiality and, predictably, ethical complexities . All of these need to be carefully managed if you choose to adopt this type of research design.

Case Study Design

With case study research design, you, as the researcher, investigate a single individual (or a single group of individuals) to gain an in-depth understanding of their experiences, behaviours or outcomes. Unlike other research designs that are aimed at larger sample sizes, case studies offer a deep dive into the specific circumstances surrounding a person, group of people, event or phenomenon, generally within a bounded setting or context .

As an example, a case study design could be used to explore the factors influencing the success of a specific small business. This would involve diving deeply into the organisation to explore and understand what makes it tick – from marketing to HR to finance. In terms of data collection, this could include interviews with staff and management, review of policy documents and financial statements, surveying customers, etc.

While the above example is focused squarely on one organisation, it’s worth noting that case study research designs can have different variation s, including single-case, multiple-case and longitudinal designs. As you can see in the example, a single-case design involves intensely examining a single entity to understand its unique characteristics and complexities. Conversely, in a multiple-case design , multiple cases are compared and contrasted to identify patterns and commonalities. Lastly, in a longitudinal case design , a single case or multiple cases are studied over an extended period of time to understand how factors develop over time.

As you can see, a case study research design is particularly useful where a deep and contextualised understanding of a specific phenomenon or issue is desired. However, this strength is also its weakness. In other words, you can’t generalise the findings from a case study to the broader population. So, keep this in mind if you’re considering going the case study route.

How To Choose A Research Design

Having worked through all of these potential research designs, you’d be forgiven for feeling a little overwhelmed and wondering, “ But how do I decide which research design to use? ”. While we could write an entire post covering that alone, here are a few factors to consider that will help you choose a suitable research design for your study.

Data type: The first determining factor is naturally the type of data you plan to be collecting – i.e., qualitative or quantitative. This may sound obvious, but we have to be clear about this – don’t try to use a quantitative research design on qualitative data (or vice versa)!

Research aim(s) and question(s): As with all methodological decisions, your research aim and research questions will heavily influence your research design. For example, if your research aims involve developing a theory from qualitative data, grounded theory would be a strong option. Similarly, if your research aims involve identifying and measuring relationships between variables, one of the experimental designs would likely be a better option.

Time: It’s essential that you consider any time constraints you have, as this will impact the type of research design you can choose. For example, if you’ve only got a month to complete your project, a lengthy design such as ethnography wouldn’t be a good fit.

Resources: Take into account the resources realistically available to you, as these need to factor into your research design choice. For example, if you require highly specialised lab equipment to execute an experimental design, you need to be sure that you’ll have access to that before you make a decision.

Keep in mind that when it comes to research, it’s important to manage your risks and play as conservatively as possible. If your entire project relies on you achieving a huge sample, having access to niche equipment or holding interviews with very difficult-to-reach participants, you’re creating risks that could kill your project. So, be sure to think through your choices carefully and make sure that you have backup plans for any existential risks. Remember that a relatively simple methodology executed well generally will typically earn better marks than a highly-complex methodology executed poorly.

Recap: Key Takeaways

We’ve covered a lot of ground here. Let’s recap by looking at the key takeaways:

• Research design refers to the overall plan, structure or strategy that guides a research project, from its conception to the final analysis of data.
• Research designs for quantitative studies include descriptive , correlational , experimental and quasi-experimenta l designs.
• Research designs for qualitative studies include phenomenological , grounded theory , ethnographic and case study designs.
• When choosing a research design, you need to consider a variety of factors, including the type of data you’ll be working with, your research aims and questions, your time and the resources available to you.

If you need a helping hand with your research design (or any other aspect of your research), check out our private coaching services .

Psst... there’s more!

This post was based on one of our popular Research Bootcamps . If you're working on a research project, you'll definitely want to check this out ...

13 Comments

Is there any blog article explaining more on Case study research design? Is there a Case study write-up template? Thank you.

Thanks this was quite valuable to clarify such an important concept.

Thanks for this simplified explanations. it is quite very helpful.

This was really helpful. thanks

Thank you for your explanation. I think case study research design and the use of secondary data in researches needs to be talked about more in your videos and articles because there a lot of case studies research design tailored projects out there.

Please is there any template for a case study research design whose data type is a secondary data on your repository?

This post is very clear, comprehensive and has been very helpful to me. It has cleared the confusion I had in regard to research design and methodology.

This post is helpful, easy to understand, and deconstructs what a research design is. Thanks

This post is really helpful.

how to cite this page

Thank you very much for the post. It is wonderful and has cleared many worries in my mind regarding research designs. I really appreciate .

how can I put this blog as my reference(APA style) in bibliography part?

This post has been very useful to me. Confusing areas have been cleared

This is very helpful and very useful!

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Methodology

• What Is a Research Design | Types, Guide & Examples

What Is a Research Design | Types, Guide & Examples

Published on June 7, 2021 by Shona McCombes . Revised on November 20, 2023 by Pritha Bhandari.

A research design is a strategy for answering your   research question  using empirical data. Creating a research design means making decisions about:

• Your overall research objectives and approach
• Whether you’ll rely on primary research or secondary research
• Your sampling methods or criteria for selecting subjects
• Your data collection methods
• The procedures you’ll follow to collect data
• Your data analysis methods

A well-planned research design helps ensure that your methods match your research objectives and that you use the right kind of analysis for your data.

Table of contents

Step 1: consider your aims and approach, step 2: choose a type of research design, step 3: identify your population and sampling method, step 4: choose your data collection methods, step 5: plan your data collection procedures, step 6: decide on your data analysis strategies, other interesting articles, frequently asked questions about research design.

• Introduction

Before you can start designing your research, you should already have a clear idea of the research question you want to investigate.

There are many different ways you could go about answering this question. Your research design choices should be driven by your aims and priorities—start by thinking carefully about what you want to achieve.

The first choice you need to make is whether you’ll take a qualitative or quantitative approach.

Qualitative research designs tend to be more flexible and inductive , allowing you to adjust your approach based on what you find throughout the research process.

Quantitative research designs tend to be more fixed and deductive , with variables and hypotheses clearly defined in advance of data collection.

It’s also possible to use a mixed-methods design that integrates aspects of both approaches. By combining qualitative and quantitative insights, you can gain a more complete picture of the problem you’re studying and strengthen the credibility of your conclusions.

Practical and ethical considerations when designing research

As well as scientific considerations, you need to think practically when designing your research. If your research involves people or animals, you also need to consider research ethics .

• How much time do you have to collect data and write up the research?
• Will you be able to gain access to the data you need (e.g., by travelling to a specific location or contacting specific people)?
• Do you have the necessary research skills (e.g., statistical analysis or interview techniques)?
• Will you need ethical approval ?

At each stage of the research design process, make sure that your choices are practically feasible.

Prevent plagiarism. Run a free check.

Within both qualitative and quantitative approaches, there are several types of research design to choose from. Each type provides a framework for the overall shape of your research.

Types of quantitative research designs

Quantitative designs can be split into four main types.

• Experimental and   quasi-experimental designs allow you to test cause-and-effect relationships
• Descriptive and correlational designs allow you to measure variables and describe relationships between them.

With descriptive and correlational designs, you can get a clear picture of characteristics, trends and relationships as they exist in the real world. However, you can’t draw conclusions about cause and effect (because correlation doesn’t imply causation ).

Experiments are the strongest way to test cause-and-effect relationships without the risk of other variables influencing the results. However, their controlled conditions may not always reflect how things work in the real world. They’re often also more difficult and expensive to implement.

Types of qualitative research designs

Qualitative designs are less strictly defined. This approach is about gaining a rich, detailed understanding of a specific context or phenomenon, and you can often be more creative and flexible in designing your research.

The table below shows some common types of qualitative design. They often have similar approaches in terms of data collection, but focus on different aspects when analyzing the data.

Your research design should clearly define who or what your research will focus on, and how you’ll go about choosing your participants or subjects.

In research, a population is the entire group that you want to draw conclusions about, while a sample is the smaller group of individuals you’ll actually collect data from.

Defining the population

A population can be made up of anything you want to study—plants, animals, organizations, texts, countries, etc. In the social sciences, it most often refers to a group of people.

For example, will you focus on people from a specific demographic, region or background? Are you interested in people with a certain job or medical condition, or users of a particular product?

The more precisely you define your population, the easier it will be to gather a representative sample.

• Sampling methods

Even with a narrowly defined population, it’s rarely possible to collect data from every individual. Instead, you’ll collect data from a sample.

To select a sample, there are two main approaches: probability sampling and non-probability sampling . The sampling method you use affects how confidently you can generalize your results to the population as a whole.

Probability sampling is the most statistically valid option, but it’s often difficult to achieve unless you’re dealing with a very small and accessible population.

For practical reasons, many studies use non-probability sampling, but it’s important to be aware of the limitations and carefully consider potential biases. You should always make an effort to gather a sample that’s as representative as possible of the population.

Case selection in qualitative research

In some types of qualitative designs, sampling may not be relevant.

For example, in an ethnography or a case study , your aim is to deeply understand a specific context, not to generalize to a population. Instead of sampling, you may simply aim to collect as much data as possible about the context you are studying.

In these types of design, you still have to carefully consider your choice of case or community. You should have a clear rationale for why this particular case is suitable for answering your research question .

For example, you might choose a case study that reveals an unusual or neglected aspect of your research problem, or you might choose several very similar or very different cases in order to compare them.

Data collection methods are ways of directly measuring variables and gathering information. They allow you to gain first-hand knowledge and original insights into your research problem.

You can choose just one data collection method, or use several methods in the same study.

Survey methods

Surveys allow you to collect data about opinions, behaviors, experiences, and characteristics by asking people directly. There are two main survey methods to choose from: questionnaires and interviews .

Observation methods

Observational studies allow you to collect data unobtrusively, observing characteristics, behaviors or social interactions without relying on self-reporting.

Observations may be conducted in real time, taking notes as you observe, or you might make audiovisual recordings for later analysis. They can be qualitative or quantitative.

Other methods of data collection

There are many other ways you might collect data depending on your field and topic.

If you’re not sure which methods will work best for your research design, try reading some papers in your field to see what kinds of data collection methods they used.

Secondary data

If you don’t have the time or resources to collect data from the population you’re interested in, you can also choose to use secondary data that other researchers already collected—for example, datasets from government surveys or previous studies on your topic.

With this raw data, you can do your own analysis to answer new research questions that weren’t addressed by the original study.

Using secondary data can expand the scope of your research, as you may be able to access much larger and more varied samples than you could collect yourself.

However, it also means you don’t have any control over which variables to measure or how to measure them, so the conclusions you can draw may be limited.

As well as deciding on your methods, you need to plan exactly how you’ll use these methods to collect data that’s consistent, accurate, and unbiased.

Planning systematic procedures is especially important in quantitative research, where you need to precisely define your variables and ensure your measurements are high in reliability and validity.

Operationalization

Some variables, like height or age, are easily measured. But often you’ll be dealing with more abstract concepts, like satisfaction, anxiety, or competence. Operationalization means turning these fuzzy ideas into measurable indicators.

If you’re using observations , which events or actions will you count?

If you’re using surveys , which questions will you ask and what range of responses will be offered?

You may also choose to use or adapt existing materials designed to measure the concept you’re interested in—for example, questionnaires or inventories whose reliability and validity has already been established.

Reliability and validity

Reliability means your results can be consistently reproduced, while validity means that you’re actually measuring the concept you’re interested in.

For valid and reliable results, your measurement materials should be thoroughly researched and carefully designed. Plan your procedures to make sure you carry out the same steps in the same way for each participant.

If you’re developing a new questionnaire or other instrument to measure a specific concept, running a pilot study allows you to check its validity and reliability in advance.

Sampling procedures

As well as choosing an appropriate sampling method , you need a concrete plan for how you’ll actually contact and recruit your selected sample.

That means making decisions about things like:

• How many participants do you need for an adequate sample size?
• What inclusion and exclusion criteria will you use to identify eligible participants?
• How will you contact your sample—by mail, online, by phone, or in person?

If you’re using a probability sampling method , it’s important that everyone who is randomly selected actually participates in the study. How will you ensure a high response rate?

If you’re using a non-probability method , how will you avoid research bias and ensure a representative sample?

Data management

It’s also important to create a data management plan for organizing and storing your data.

Will you need to transcribe interviews or perform data entry for observations? You should anonymize and safeguard any sensitive data, and make sure it’s backed up regularly.

Keeping your data well-organized will save time when it comes to analyzing it. It can also help other researchers validate and add to your findings (high replicability ).

On its own, raw data can’t answer your research question. The last step of designing your research is planning how you’ll analyze the data.

Quantitative data analysis

In quantitative research, you’ll most likely use some form of statistical analysis . With statistics, you can summarize your sample data, make estimates, and test hypotheses.

Using descriptive statistics , you can summarize your sample data in terms of:

• The distribution of the data (e.g., the frequency of each score on a test)
• The central tendency of the data (e.g., the mean to describe the average score)
• The variability of the data (e.g., the standard deviation to describe how spread out the scores are)

The specific calculations you can do depend on the level of measurement of your variables.

Using inferential statistics , you can:

• Make estimates about the population based on your sample data.
• Test hypotheses about a relationship between variables.

Regression and correlation tests look for associations between two or more variables, while comparison tests (such as t tests and ANOVAs ) look for differences in the outcomes of different groups.

Your choice of statistical test depends on various aspects of your research design, including the types of variables you’re dealing with and the distribution of your data.

Qualitative data analysis

In qualitative research, your data will usually be very dense with information and ideas. Instead of summing it up in numbers, you’ll need to comb through the data in detail, interpret its meanings, identify patterns, and extract the parts that are most relevant to your research question.

Two of the most common approaches to doing this are thematic analysis and discourse analysis .

There are many other ways of analyzing qualitative data depending on the aims of your research. To get a sense of potential approaches, try reading some qualitative research papers in your field.

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

• Simple random sampling
• Stratified sampling
• Cluster sampling
• Likert scales
• Reproducibility

 Statistics

• Null hypothesis
• Statistical power
• Probability distribution
• Effect size
• Poisson distribution

Research bias

• Optimism bias
• Cognitive bias
• Implicit bias
• Hawthorne effect
• Anchoring bias
• Explicit bias

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

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

Quantitative research designs can be divided into two main categories:

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

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

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

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

A sample is a subset of individuals from a larger population . Sampling means selecting the group that you will actually collect data from in your research. For example, if you are researching the opinions of students in your university, you could survey a sample of 100 students.

In statistics, sampling allows you to test a hypothesis about the characteristics of a population.

Operationalization means turning abstract conceptual ideas into measurable observations.

For example, the concept of social anxiety isn’t directly observable, but it can be operationally defined in terms of self-rating scores, behavioral avoidance of crowded places, or physical anxiety symptoms in social situations.

Before collecting data , it’s important to consider how you will operationalize the variables that you want to measure.

A research project is an academic, scientific, or professional undertaking to answer a research question . Research projects can take many forms, such as qualitative or quantitative , descriptive , longitudinal , experimental , or correlational . What kind of research approach you choose will depend on your topic.

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Single-Case Experimental Designs: A Systematic Review of Published Research and Current Standards

Justin d. smith.

Child and Family Center, University of Oregon

This article systematically reviews the research design and methodological characteristics of single-case experimental design (SCED) research published in peer-reviewed journals between 2000 and 2010. SCEDs provide researchers with a flexible and viable alternative to group designs with large sample sizes. However, methodological challenges have precluded widespread implementation and acceptance of the SCED as a viable complementary methodology to the predominant group design. This article includes a description of the research design, measurement, and analysis domains distinctive to the SCED; a discussion of the results within the framework of contemporary standards and guidelines in the field; and a presentation of updated benchmarks for key characteristics (e.g., baseline sampling, method of analysis), and overall, it provides researchers and reviewers with a resource for conducting and evaluating SCED research. The results of the systematic review of 409 studies suggest that recently published SCED research is largely in accordance with contemporary criteria for experimental quality. Analytic method emerged as an area of discord. Comparison of the findings of this review with historical estimates of the use of statistical analysis indicates an upward trend, but visual analysis remains the most common analytic method and also garners the most support amongst those entities providing SCED standards. Although consensus exists along key dimensions of single-case research design and researchers appear to be practicing within these parameters, there remains a need for further evaluation of assessment and sampling techniques and data analytic methods.

The single-case experiment has a storied history in psychology dating back to the field’s founders: Fechner (1889) , Watson (1925) , and Skinner (1938) . It has been used to inform and develop theory, examine interpersonal processes, study the behavior of organisms, establish the effectiveness of psychological interventions, and address a host of other research questions (for a review, see Morgan & Morgan, 2001 ). In recent years the single-case experimental design (SCED) has been represented in the literature more often than in past decades, as is evidenced by recent reviews ( Hammond & Gast, 2010 ; Shadish & Sullivan, 2011 ), but it still languishes behind the more prominent group design in nearly all subfields of psychology. Group designs are often professed to be superior because they minimize, although do not necessarily eliminate, the major internal validity threats to drawing scientifically valid inferences from the results ( Shadish, Cook, & Campbell, 2002 ). SCEDs provide a rigorous, methodologically sound alternative method of evaluation (e.g., Barlow, Nock, & Hersen, 2008 ; Horner et al., 2005 ; Kazdin, 2010 ; Kratochwill & Levin, 2010 ; Shadish et al., 2002 ) but are often overlooked as a true experimental methodology capable of eliciting legitimate inferences (e.g., Barlow et al., 2008 ; Kazdin, 2010 ). Despite a shift in the zeitgeist from single-case experiments to group designs more than a half century ago, recent and rapid methodological advancements suggest that SCEDs are poised for resurgence.

Single case refers to the participant or cluster of participants (e.g., a classroom, hospital, or neighborhood) under investigation. In contrast to an experimental group design in which one group is compared with another, participants in a single-subject experiment research provide their own control data for the purpose of comparison in a within-subject rather than a between-subjects design. SCEDs typically involve a comparison between two experimental time periods, known as phases. This approach typically includes collecting a representative baseline phase to serve as a comparison with subsequent phases. In studies examining single subjects that are actually groups (i.e., classroom, school), there are additional threats to internal validity of the results, as noted by Kratochwill and Levin (2010) , which include setting or site effects.

The central goal of the SCED is to determine whether a causal or functional relationship exists between a researcher-manipulated independent variable (IV) and a meaningful change in the dependent variable (DV). SCEDs generally involve repeated, systematic assessment of one or more IVs and DVs over time. The DV is measured repeatedly across and within all conditions or phases of the IV. Experimental control in SCEDs includes replication of the effect either within or between participants ( Horner et al., 2005 ). Randomization is another way in which threats to internal validity can be experimentally controlled. Kratochwill and Levin (2010) recently provided multiple suggestions for adding a randomization component to SCEDs to improve the methodological rigor and internal validity of the findings.

Examination of the effectiveness of interventions is perhaps the area in which SCEDs are most well represented ( Morgan & Morgan, 2001 ). Researchers in behavioral medicine and in clinical, health, educational, school, sport, rehabilitation, and counseling psychology often use SCEDs because they are particularly well suited to examining the processes and outcomes of psychological and behavioral interventions (e.g., Borckardt et al., 2008 ; Kazdin, 2010 ; Robey, Schultz, Crawford, & Sinner, 1999 ). Skepticism about the clinical utility of the randomized controlled trial (e.g., Jacobsen & Christensen, 1996 ; Wachtel, 2010 ; Westen & Bradley, 2005 ; Westen, Novotny, & Thompson-Brenner, 2004 ) has renewed researchers’ interest in SCEDs as a means to assess intervention outcomes (e.g., Borckardt et al., 2008 ; Dattilio, Edwards, & Fishman, 2010 ; Horner et al., 2005 ; Kratochwill, 2007 ; Kratochwill & Levin, 2010 ). Although SCEDs are relatively well represented in the intervention literature, it is by no means their sole home: Examples appear in nearly every subfield of psychology (e.g., Bolger, Davis, & Rafaeli, 2003 ; Piasecki, Hufford, Solham, & Trull, 2007 ; Reis & Gable, 2000 ; Shiffman, Stone, & Hufford, 2008 ; Soliday, Moore, & Lande, 2002 ). Aside from the current preference for group-based research designs, several methodological challenges have repressed the proliferation of the SCED.

Methodological Complexity

SCEDs undeniably present researchers with a complex array of methodological and research design challenges, such as establishing a representative baseline, managing the nonindependence of sequential observations (i.e., autocorrelation, serial dependence), interpreting single-subject effect sizes, analyzing the short data streams seen in many applications, and appropriately addressing the matter of missing observations. In the field of intervention research for example, Hser et al. (2001) noted that studies using SCEDs are “rare” because of the minimum number of observations that are necessary (e.g., 3–5 data points in each phase) and the complexity of available data analysis approaches. Advances in longitudinal person-based trajectory analysis (e.g., Nagin, 1999 ), structural equation modeling techniques (e.g., Lubke & Muthén, 2005 ), time-series forecasting (e.g., autoregressive integrated moving averages; Box & Jenkins, 1970 ), and statistical programs designed specifically for SCEDs (e.g., Simulation Modeling Analysis; Borckardt, 2006 ) have provided researchers with robust means of analysis, but they might not be feasible methods for the average psychological scientist.

Application of the SCED has also expanded. Today, researchers use variants of the SCED to examine complex psychological processes and the relationship between daily and momentary events in peoples’ lives and their psychological correlates. Research in nearly all subfields of psychology has begun to use daily diary and ecological momentary assessment (EMA) methods in the context of the SCED, opening the door to understanding increasingly complex psychological phenomena (see Bolger et al., 2003 ; Shiffman et al., 2008 ). In contrast to the carefully controlled laboratory experiment that dominated research in the first half of the twentieth century (e.g., Skinner, 1938 ; Watson, 1925 ), contemporary proponents advocate application of the SCED in naturalistic studies to increase the ecological validity of empirical findings (e.g., Bloom, Fisher, & Orme, 2003 ; Borckardt et al., 2008 ; Dattilio et al., 2010 ; Jacobsen & Christensen, 1996 ; Kazdin, 2008 ; Morgan & Morgan, 2001 ; Westen & Bradley, 2005 ; Westen et al., 2004 ). Recent advancements and expanded application of SCEDs indicate a need for updated design and reporting standards.

Many current benchmarks in the literature concerning key parameters of the SCED were established well before current advancements and innovations, such as the suggested minimum number of data points in the baseline phase(s), which remains a disputed area of SCED research (e.g., Center, Skiba, & Casey, 1986 ; Huitema, 1985 ; R. R. Jones, Vaught, & Weinrott, 1977 ; Sharpley, 1987 ). This article comprises (a) an examination of contemporary SCED methodological and reporting standards; (b) a systematic review of select design, measurement, and statistical characteristics of published SCED research during the past decade; and (c) a broad discussion of the critical aspects of this research to inform methodological improvements and study reporting standards. The reader will garner a fundamental understanding of what constitutes appropriate methodological soundness in single-case experimental research according to the established standards in the field, which can be used to guide the design of future studies, improve the presentation of publishable empirical findings, and inform the peer-review process. The discussion begins with the basic characteristics of the SCED, including an introduction to time-series, daily diary, and EMA strategies, and describes how current reporting and design standards apply to each of these areas of single-case research. Interweaved within this presentation are the results of a systematic review of SCED research published between 2000 and 2010 in peer-reviewed outlets and a discussion of the way in which these findings support, or differ from, existing design and reporting standards and published SCED benchmarks.

Review of Current SCED Guidelines and Reporting Standards

In contrast to experimental group comparison studies, which conform to generally well agreed upon methodological design and reporting guidelines, such as the CONSORT ( Moher, Schulz, Altman, & the CONSORT Group, 2001 ) and TREND ( Des Jarlais, Lyles, & Crepaz, 2004 ) statements for randomized and nonrandomized trials, respectively, there is comparatively much less consensus when it comes to the SCED. Until fairly recently, design and reporting guidelines for single-case experiments were almost entirely absent in the literature and were typically determined by the preferences of a research subspecialty or a particular journal’s editorial board. Factions still exist within the larger field of psychology, as can be seen in the collection of standards presented in this article, particularly in regard to data analytic methods of SCEDs, but fortunately there is budding agreement about certain design and measurement characteristics. A number of task forces, professional groups, and independent experts in the field have recently put forth guidelines; each has a relatively distinct purpose, which likely accounts for some of the discrepancies between them. In what is to be a central theme of this article, researchers are ultimately responsible for thoughtfully and synergistically combining research design, measurement, and analysis aspects of a study.

This review presents the more prominent, comprehensive, and recently established SCED standards. Six sources are discussed: (1) Single-Case Design Technical Documentation from the What Works Clearinghouse (WWC; Kratochwill et al., 2010 ); (2) the APA Division 12 Task Force on Psychological Interventions, with contributions from the Division 12 Task Force on Promotion and Dissemination of Psychological Procedures and the APA Task Force for Psychological Intervention Guidelines (DIV12; presented in Chambless & Hollon, 1998 ; Chambless & Ollendick, 2001 ), adopted and expanded by APA Division 53, the Society for Clinical Child and Adolescent Psychology ( Weisz & Hawley, 1998 , 1999 ); (3) the APA Division 16 Task Force on Evidence-Based Interventions in School Psychology (DIV16; Members of the Task Force on Evidence-Based Interventions in School Psychology. Chair: T. R. Kratochwill, 2003); (4) the National Reading Panel (NRP; National Institute of Child Health and Human Development, 2000 ); (5) the Single-Case Experimental Design Scale ( Tate et al., 2008 ); and (6) the reporting guidelines for EMA put forth by Stone & Shiffman (2002) . Although the specific purposes of each source differ somewhat, the overall aim is to provide researchers and reviewers with agreed-upon criteria to be used in the conduct and evaluation of SCED research. The standards provided by WWC, DIV12, DIV16, and the NRP represent the efforts of task forces. The Tate et al. scale was selected for inclusion in this review because it represents perhaps the only psychometrically validated tool for assessing the rigor of SCED methodology. Stone and Shiffman’s (2002) standards were intended specifically for EMA methods, but many of their criteria also apply to time-series, daily diary, and other repeated-measurement and sampling methods, making them pertinent to this article. The design, measurement, and analysis standards are presented in the later sections of this article and notable concurrences, discrepancies, strengths, and deficiencies are summarized.

Systematic Review Search Procedures and Selection Criteria

Search strategy.

A comprehensive search strategy of SCEDs was performed to identify studies published in peer-reviewed journals meeting a priori search and inclusion criteria. First, a computer-based PsycINFO search of articles published between 2000 and 2010 (search conducted in July 2011) was conducted that used the following primary key terms and phrases that appeared anywhere in the article (asterisks denote that any characters/letters can follow the last character of the search term): alternating treatment design, changing criterion design, experimental case*, multiple baseline design, replicated single-case design, simultaneous treatment design, time-series design. The search was limited to studies published in the English language and those appearing in peer-reviewed journals within the specified publication year range. Additional limiters of the type of article were also used in PsycINFO to increase specificity: The search was limited to include methodologies indexed as either quantitative study OR treatment outcome/randomized clinical trial and NOT field study OR interview OR focus group OR literature review OR systematic review OR mathematical model OR qualitative study.

Study selection

The author used a three-phase study selection, screening, and coding procedure to select the highest number of applicable studies. Phase 1 consisted of the initial systematic review conducted using PsycINFO, which resulted in 571 articles. In Phase 2, titles and abstracts were screened: Articles appearing to use a SCED were retained (451) for Phase 3, in which the author and a trained research assistant read each full-text article and entered the characteristics of interest into a database. At each phase of the screening process, studies that did not use a SCED or that either self-identified as, or were determined to be, quasi-experimental were dropped. Of the 571 original studies, 82 studies were determined to be quasi-experimental. The definition of a quasi-experimental design used in the screening procedure conforms to the descriptions provided by Kazdin (2010) and Shadish et al. (2002) regarding the necessary components of an experimental design. For example, reversal designs require a minimum of four phases (e.g., ABAB), and multiple baseline designs must demonstrate replication of the effect across at least three conditions (e.g., subjects, settings, behaviors). Sixteen studies were unavailable in full text in English, and five could not be obtained in full text and were thus dropped. The remaining articles that were not retained for review (59) were determined not to be SCED studies meeting our inclusion criteria, but had been identified in our PsycINFO search using the specified keyword and methodology terms. For this review, 409 studies were selected. The sources of the 409 reviewed studies are summarized in Table 1 . A complete bibliography of the 571 studies appearing in the initial search, with the included studies marked, is available online as an Appendix or from the author.

Journal Sources of Studies Included in the Systematic Review (N = 409)

Note: Each of the following journal titles contributed 1 study unless otherwise noted in parentheses: Augmentative and Alternative Communication; Acta Colombiana de Psicología; Acta Comportamentalia; Adapted Physical Activity Quarterly (2); Addiction Research and Theory; Advances in Speech Language Pathology; American Annals of the Deaf; American Journal of Education; American Journal of Occupational Therapy; American Journal of Speech-Language Pathology; The American Journal on Addictions; American Journal on Mental Retardation; Applied Ergonomics; Applied Psychophysiology and Biofeedback; Australian Journal of Guidance & Counseling; Australian Psychologist; Autism; The Behavior Analyst; The Behavior Analyst Today; Behavior Analysis in Practice (2); Behavior and Social Issues (2); Behaviour Change (2); Behavioural and Cognitive Psychotherapy; Behaviour Research and Therapy (3); Brain and Language (2); Brain Injury (2); Canadian Journal of Occupational Therapy (2); Canadian Journal of School Psychology; Career Development for Exceptional Individuals; Chinese Mental Health Journal; Clinical Linguistics and Phonetics; Clinical Psychology & Psychotherapy; Cognitive and Behavioral Practice; Cognitive Computation; Cognitive Therapy and Research; Communication Disorders Quarterly; Developmental Medicine & Child Neurology (2); Developmental Neurorehabilitation (2); Disability and Rehabilitation: An International, Multidisciplinary Journal (3); Disability and Rehabilitation: Assistive Technology; Down Syndrome: Research & Practice; Drug and Alcohol Dependence (2); Early Childhood Education Journal (2); Early Childhood Services: An Interdisciplinary Journal of Effectiveness; Educational Psychology (2); Education and Training in Autism and Developmental Disabilities; Electronic Journal of Research in Educational Psychology; Environment and Behavior (2); European Eating Disorders Review; European Journal of Sport Science; European Review of Applied Psychology; Exceptional Children; Exceptionality; Experimental and Clinical Psychopharmacology; Family & Community Health: The Journal of Health Promotion & Maintenance; Headache: The Journal of Head and Face Pain; International Journal of Behavioral Consultation and Therapy (2); International Journal of Disability; Development and Education (2); International Journal of Drug Policy; International Journal of Psychology; International Journal of Speech-Language Pathology; International Psychogeriatrics; Japanese Journal of Behavior Analysis (3); Japanese Journal of Special Education; Journal of Applied Research in Intellectual Disabilities (2); Journal of Applied Sport Psychology (3); Journal of Attention Disorders (2); Journal of Behavior Therapy and Experimental Psychiatry; Journal of Child Psychology and Psychiatry; Journal of Clinical Psychology in Medical Settings; Journal of Clinical Sport Psychology; Journal of Cognitive Psychotherapy; Journal of Consulting and Clinical Psychology (2); Journal of Deaf Studies and Deaf Education; Journal of Educational & Psychological Consultation (2); Journal of Evidence-Based Practices for Schools (2); Journal of the Experimental Analysis of Behavior (2); Journal of General Internal Medicine; Journal of Intellectual and Developmental Disabilities; Journal of Intellectual Disability Research (2); Journal of Medical Speech-Language Pathology; Journal of Neurology, Neurosurgery & Psychiatry; Journal of Paediatrics and Child Health; Journal of Prevention and Intervention in the Community; Journal of Safety Research; Journal of School Psychology (3); The Journal of Socio-Economics; The Journal of Special Education; Journal of Speech, Language, and Hearing Research (2); Journal of Sport Behavior; Journal of Substance Abuse Treatment; Journal of the International Neuropsychological Society; Journal of Traumatic Stress; The Journals of Gerontology: Series B: Psychological Sciences and Social Sciences; Language, Speech, and Hearing Services in Schools; Learning Disabilities Research & Practice (2); Learning Disability Quarterly (2); Music Therapy Perspectives; Neurorehabilitation and Neural Repair; Neuropsychological Rehabilitation (2); Pain; Physical Education and Sport Pedagogy (2); Preventive Medicine: An International Journal Devoted to Practice and Theory; Psychological Assessment; Psychological Medicine: A Journal of Research in Psychiatry and the Allied Sciences; The Psychological Record; Reading and Writing; Remedial and Special Education (3); Research and Practice for Persons with Severe Disabilities (2); Restorative Neurology and Neuroscience; School Psychology International; Seminars in Speech and Language; Sleep and Hypnosis; School Psychology Quarterly; Social Work in Health Care; The Sport Psychologist (3); Therapeutic Recreation Journal (2); The Volta Review; Work: Journal of Prevention, Assessment & Rehabilitation.

Coding criteria amplifications

A comprehensive description of the coding criteria for each category in this review is available from the author by request. The primary coding criteria are described here and in later sections of this article.

• Research design was classified into one of the types discussed later in the section titled Predominant Single-Case Experimental Designs on the basis of the authors’ stated design type. Secondary research designs were then coded when applicable (i.e., mixed designs). Distinctions between primary and secondary research designs were made based on the authors’ description of their study. For example, if an author described the study as a “multiple baseline design with time-series measurement,” the primary research design would be coded as being multiple baseline, and time-series would be coded as the secondary research design.
• Observer ratings were coded as present when observational coding procedures were described and/or the results of a test of interobserver agreement were reported.
• Interrater reliability for observer ratings was coded as present in any case in which percent agreement, alpha, kappa, or another appropriate statistic was reported, regardless of the amount of the total data that were examined for agreement.
• Daily diary, daily self-report, and EMA codes were given when authors explicitly described these procedures in the text by name. Coders did not infer the use of these measurement strategies.
• The number of baseline observations was either taken directly from the figures provided in text or was simply counted in graphical displays of the data when this was determined to be a reliable approach. In some cases, it was not possible to reliably determine the number of baseline data points from the graphical display of data, in which case, the “unavailable” code was assigned. Similarly, the “unavailable” code was assigned when the number of observations was either unreported or ambiguous, or only a range was provided and thus no mean could be determined. Similarly, the mean number of baseline observations was calculated for each study prior to further descriptive statistical analyses because a number of studies reported means only.
• The coding of the analytic method used in the reviewed studies is discussed later in the section titled Discussion of Review Results and Coding of Analytic Methods .

Results of the Systematic Review

Descriptive statistics of the design, measurement, and analysis characteristics of the reviewed studies are presented in Table 2 . The results and their implications are discussed in the relevant sections throughout the remainder of the article.

Descriptive Statistics of Reviewed SCED Characteristics

Note. % refers to the proportion of reviewed studies that satisfied criteria for this code: For example, the percent of studies reporting observer ratings.

Discussion of the Systematic Review Results in Context

The SCED is a very flexible methodology and has many variants. Those mentioned here are the building blocks from which other designs are then derived. For those readers interested in the nuances of each design, Barlow et al., (2008) ; Franklin, Allison, and Gorman (1997) ; Kazdin (2010) ; and Kratochwill and Levin (1992) , among others, provide cogent, in-depth discussions. Identifying the appropriate SCED depends upon many factors, including the specifics of the IV, the setting in which the study will be conducted, participant characteristics, the desired or hypothesized outcomes, and the research question(s). Similarly, the researcher’s selection of measurement and analysis techniques is determined by these factors.

Predominant Single-Case Experimental Designs

Alternating/simultaneous designs (6%; primary design of the studies reviewed).

Alternating and simultaneous designs involve an iterative manipulation of the IV(s) across different phases to show that changes in the DV vary systematically as a function of manipulating the IV(s). In these multielement designs, the researcher has the option to alternate the introduction of two or more IVs or present two or more IVs at the same time. In the alternating variation, the researcher is able to determine the relative impact of two different IVs on the DV, when all other conditions are held constant. Another variation of this design is to alternate IVs across various conditions that could be related to the DV (e.g., class period, interventionist). Similarly, the simultaneous design would occur when the IVs were presented at the same time within the same phase of the study.

Changing criterion design (4%)

Changing criterion designs are used to demonstrate a gradual change in the DV over the course of the phase involving the active manipulation of the IV. Criteria indicating that a change has occurred happen in a step-wise manner, in which the criterion shifts as the participant responds to the presence of the manipulated IV. The changing criterion design is particularly useful in applied intervention research for a number of reasons. The IV is continuous and never withdrawn, unlike the strategy used in a reversal design. This is particularly important in situations where removal of a psychological intervention would be either detrimental or dangerous to the participant, or would be otherwise unfeasible or unethical. The multiple baseline design also does not withdraw intervention, but it requires replicating the effects of the intervention across participants, settings, or situations. A changing criterion design can be accomplished with one participant in one setting without withholding or withdrawing treatment.

Multiple baseline/combined series design (69%)

The multiple baseline or combined series design can be used to test within-subject change across conditions and often involves multiple participants in a replication context. The multiple baseline design is quite simple in many ways, essentially consisting of a number of repeated, miniature AB experiments or variations thereof. Introduction of the IV is staggered temporally across multiple participants or across multiple within-subject conditions, which allows the researcher to demonstrate that changes in the DV reliably occur only when the IV is introduced, thus controlling for the effects of extraneous factors. Multiple baseline designs can be used both within and across units (i.e., persons or groups of persons). When the baseline phase of each subject begins simultaneously, it is called a concurrent multiple baseline design. In a nonconcurrent variation, baseline periods across subjects begin at different points in time. The multiple baseline design is useful in many settings in which withdrawal of the IV would not be appropriate or when introduction of the IV is hypothesized to result in permanent change that would not reverse when the IV is withdrawn. The major drawback of this design is that the IV must be initially withheld for a period of time to ensure different starting points across the different units in the baseline phase. Depending upon the nature of the research questions, withholding an IV, such as a treatment, could be potentially detrimental to participants.

Reversal designs (17%)

Reversal designs are also known as introduction and withdrawal and are denoted as ABAB designs in their simplest form. As the name suggests, the reversal design involves collecting a baseline measure of the DV (the first A phase), introducing the IV (the first B phase), removing the IV while continuing to assess the DV (the second A phase), and then reintroducing the IV (the second B phase). This pattern can be repeated as many times as is necessary to demonstrate an effect or otherwise address the research question. Reversal designs are useful when the manipulation is hypothesized to result in changes in the DV that are expected to reverse or discontinue when the manipulation is not present. Maintenance of an effect is often necessary to uphold the findings of reversal designs. The demonstration of an effect is evident in reversal designs when improvement occurs during the first manipulation phase, compared to the first baseline phase, then reverts to or approaches original baseline levels during the second baseline phase when the manipulation has been withdrawn, and then improves again when the manipulation in then reinstated. This pattern of reversal, when the manipulation is introduced and then withdrawn, is essential to attributing changes in the DV to the IV. However, maintenance of the effects in a reversal design, in which the DV is hypothesized to reverse when the IV is withdrawn, is not incompatible ( Kazdin, 2010 ). Maintenance is demonstrated by repeating introduction–withdrawal segments until improvement in the DV becomes permanent even when the IV is withdrawn. There is not always a need to demonstrate maintenance in all applications, nor is it always possible or desirable, but it is paramount in the learning and intervention research contexts.

Mixed designs (10%)

Mixed designs include a combination of more than one SCED (e.g., a reversal design embedded within a multiple baseline) or an SCED embedded within a group design (i.e., a randomized controlled trial comparing two groups of multiple baseline experiments). Mixed designs afford the researcher even greater flexibility in designing a study to address complex psychological hypotheses, but also capitalize on the strengths of the various designs. See Kazdin (2010) for a discussion of the variations and utility of mixed designs.

Related Nonexperimental Designs

Quasi-experimental designs.

In contrast to the designs previously described, all of which constitute “true experiments” ( Kazdin, 2010 ; Shadish et al., 2002 ), in quasi-experimental designs the conditions of a true experiment (e.g., active manipulation of the IV, replication of the effect) are approximated and are not readily under the control of the researcher. Because the focus of this article is on experimental designs, quasi-experiments are not discussed in detail; instead the reader is referred to Kazdin (2010) and Shadish et al. (2002) .

Ecological and naturalistic single-case designs

For a single-case design to be experimental, there must be active manipulation of the IV, but in some applications, such as those that might be used in social and personality psychology, the researcher might be interested in measuring naturally occurring phenomena and examining their temporal relationships. Thus, the researcher will not use a manipulation. An example of this type of research might be a study about the temporal relationship between alcohol consumption and depressed mood, which can be measured reliably using EMA methods. Psychotherapy process researchers also use this type of design to assess dyadic relationship dynamics between therapists and clients (e.g., Tschacher & Ramseyer, 2009 ).

Research Design Standards

Each of the reviewed standards provides some degree of direction regarding acceptable research designs. The WWC provides the most detailed and specific requirements regarding design characteristics. Those guidelines presented in Tables 3 , ​ ,4, 4 , and ​ and5 5 are consistent with the methodological rigor necessary to meet the WWC distinction “meets standards.” The WWC also provides less-stringent standards for a “meets standards with reservations” distinction. When minimum criteria in the design, measurement, or analysis sections of a study are not met, it is rated “does not meet standards” ( Kratochwill et al., 2010 ). Many SCEDs are acceptable within the standards of DIV12, DIV16, NRP, and in the Tate et al. SCED scale. DIV12 specifies that replication occurs across a minimum of three successive cases, which differs from the WWC specifications, which allow for three replications within a single-subject design but does not necessarily need to be across multiple subjects. DIV16 does not require, but seems to prefer, a multiple baseline design with a between-subject replication. Tate et al. state that the “design allows for the examination of cause and effect relationships to demonstrate efficacy” (p. 400, 2008). Determining whether or not a design meets this requirement is left up to the evaluator, who might then refer to one of the other standards or another source for direction.

Research Design Standards and Guidelines

Measurement and Assessment Standards and Guidelines

Analysis Standards and Guidelines

The Stone and Shiffman (2002) standards for EMA are concerned almost entirely with the reporting of measurement characteristics and less so with research design. One way in which these standards differ from those of other sources is in the active manipulation of the IV. Many research questions in EMA, daily diary, and time-series designs are concerned with naturally occurring phenomena, and a researcher manipulation would run counter to this aim. The EMA standards become important when selecting an appropriate measurement strategy within the SCED. In EMA applications, as is also true in some other time-series and daily diary designs, researcher manipulation occurs as a function of the sampling interval in which DVs of interest are measured according to fixed time schedules (e.g., reporting occurs at the end of each day), random time schedules (e.g., the data collection device prompts the participant to respond at random intervals throughout the day), or on an event-based schedule (e.g., reporting occurs after a specified event takes place).

Measurement

The basic measurement requirement of the SCED is a repeated assessment of the DV across each phase of the design in order to draw valid inferences regarding the effect of the IV on the DV. In other applications, such as those used by personality and social psychology researchers to study various human phenomena ( Bolger et al., 2003 ; Reis & Gable, 2000 ), sampling strategies vary widely depending on the topic area under investigation. Regardless of the research area, SCEDs are most typically concerned with within-person change and processes and involve a time-based strategy, most commonly to assess global daily averages or peak daily levels of the DV. Many sampling strategies, such as time-series, in which reporting occurs at uniform intervals or on event-based, fixed, or variable schedules, are also appropriate measurement methods and are common in psychological research (see Bolger et al., 2003 ).

Repeated-measurement methods permit the natural, even spontaneous, reporting of information ( Reis, 1994 ), which reduces the biases of retrospection by minimizing the amount of time elapsed between an experience and the account of this experience ( Bolger et al., 2003 ). Shiffman et al. (2008) aptly noted that the majority of research in the field of psychology relies heavily on retrospective assessment measures, even though retrospective reports have been found to be susceptible to state-congruent recall (e.g., Bower, 1981 ) and a tendency to report peak levels of the experience instead of giving credence to temporal fluctuations ( Redelmeier & Kahneman, 1996 ; Stone, Broderick, Kaell, Deles-Paul, & Porter, 2000 ). Furthermore, Shiffman et al. (1997) demonstrated that subjective aggregate accounts were a poor fit to daily reported experiences, which can be attributed to reductions in measurement error resulting in increased validity and reliability of the daily reports.

The necessity of measuring at least one DV repeatedly means that the selected assessment method, instrument, and/or construct must be sensitive to change over time and be capable of reliably and validly capturing change. Horner et al. (2005) discusses the important features of outcome measures selected for use in these types of designs. Kazdin (2010) suggests that measures be dimensional, which can more readily detect effects than categorical and binary measures. Although using an established measure or scale, such as the Outcome Questionnaire System ( M. J. Lambert, Hansen, & Harmon, 2010 ), provides empirically validated items for assessing various outcomes, most measure validation studies conducted on this type of instrument involve between-subject designs, which is no guarantee that these measures are reliable and valid for assessing within-person variability. Borsboom, Mellenbergh, and van Heerden (2003) suggest that researchers adapting validated measures should consider whether the items they propose using have a factor structure within subjects similar to that obtained between subjects. This is one of the reasons that SCEDs often use observational assessments from multiple sources and report the interrater reliability of the measure. Self-report measures are acceptable practice in some circles, but generally additional assessment methods or informants are necessary to uphold the highest methodological standards. The results of this review indicate that the majority of studies include observational measurement (76.0%). Within those studies, nearly all (97.1%) reported interrater reliability procedures and results. The results within each design were similar, with the exception of time-series designs, which used observer ratings in only half of the reviewed studies.

Time-series

Time-series designs are defined by repeated measurement of variables of interest over a period of time ( Box & Jenkins, 1970 ). Time-series measurement most often occurs in uniform intervals; however, this is no longer a constraint of time-series designs (see Harvey, 2001 ). Although uniform interval reporting is not necessary in SCED research, repeated measures often occur at uniform intervals, such as once each day or each week, which constitutes a time-series design. The time-series design has been used in various basic science applications ( Scollon, Kim-Pietro, & Diener, 2003 ) across nearly all subspecialties in psychology (e.g., Bolger et al., 2003 ; Piasecki et al., 2007 ; for a review, see Reis & Gable, 2000 ; Soliday et al., 2002 ). The basic time-series formula for a two-phase (AB) data stream is presented in Equation 1 . In this formula α represents the step function of the data stream; S represents the change between the first and second phases, which is also the intercept in a two-phase data stream and a step function being 0 at times i = 1, 2, 3…n1 and 1 at times i = n1+1, n1+2, n1+3…n; n 1 is the number of observations in the baseline phase; n is the total number of data points in the data stream; i represents time; and ε i = ρε i −1 + e i , which indicates the relationship between the autoregressive function (ρ) and the distribution of the data in the stream.

Time-series formulas become increasingly complex when seasonality and autoregressive processes are modeled in the analytic procedures, but these are rarely of concern for short time-series data streams in SCEDs. For a detailed description of other time-series design and analysis issues, see Borckardt et al. (2008) , Box and Jenkins (1970) , Crosbie (1993) , R. R. Jones et al. (1977) , and Velicer and Fava (2003) .

Time-series and other repeated-measures methodologies also enable examination of temporal effects. Borckardt et al. (2008) and others have noted that time-series designs have the potential to reveal how change occurs, not simply if it occurs. This distinction is what most interested Skinner (1938) , but it often falls below the purview of today’s researchers in favor of group designs, which Skinner felt obscured the process of change. In intervention and psychopathology research, time-series designs can assess mediators of change ( Doss & Atkins, 2006 ), treatment processes ( Stout, 2007 ; Tschacher & Ramseyer, 2009 ), and the relationship between psychological symptoms (e.g., Alloy, Just, & Panzarella, 1997 ; Hanson & Chen, 2010 ; Oslin, Cary, Slaymaker, Colleran, & Blow, 2009 ), and might be capable of revealing mechanisms of change ( Kazdin, 2007 , 2009 , 2010 ). Between- and within-subject SCED designs with repeated measurements enable researchers to examine similarities and differences in the course of change, both during and as a result of manipulating an IV. Temporal effects have been largely overlooked in many areas of psychological science ( Bolger et al., 2003 ): Examining temporal relationships is sorely needed to further our understanding of the etiology and amplification of numerous psychological phenomena.

Time-series studies were very infrequently found in this literature search (2%). Time-series studies traditionally occur in subfields of psychology in which single-case research is not often used (e.g., personality, physiological/biological). Recent advances in methods for collecting and analyzing time-series data (e.g., Borckardt et al., 2008 ) could expand the use of time-series methodology in the SCED community. One problem with drawing firm conclusions from this particular review finding is a semantic factor: Time-series is a specific term reserved for measurement occurring at a uniform interval. However, SCED research appears to not yet have adopted this language when referring to data collected in this fashion. When time-series data analytic methods are not used, the matter of measurement interval is of less importance and might not need to be specified or described as a time-series. An interesting extension of this work would be to examine SCED research that used time-series measurement strategies but did not label it as such. This is important because then it could be determined how many SCEDs could be analyzed with time-series statistical methods.

Daily diary and ecological momentary assessment methods

EMA and daily diary approaches represent methodological procedures for collecting repeated measurements in time-series and non-time-series experiments, which are also known as experience sampling. Presenting an in-depth discussion of the nuances of these sampling techniques is well beyond the scope of this paper. The reader is referred to the following review articles: daily diary ( Bolger et al., 2003 ; Reis & Gable, 2000 ; Thiele, Laireiter, & Baumann, 2002 ), and EMA ( Shiffman et al., 2008 ). Experience sampling in psychology has burgeoned in the past two decades as technological advances have permitted more precise and immediate reporting by participants (e.g., Internet-based, two-way pagers, cellular telephones, handheld computers) than do paper and pencil methods (for reviews see Barrett & Barrett, 2001 ; Shiffman & Stone, 1998 ). Both methods have practical limitations and advantages. For example, electronic methods are more costly and may exclude certain subjects from participating in the study, either because they do not have access to the necessary technology or they do not have the familiarity or savvy to successfully complete reporting. Electronic data collection methods enable the researcher to prompt responses at random or predetermined intervals and also accurately assess compliance. Paper and pencil methods have been criticized for their inability to reliably track respondents’ compliance: Palermo, Valenzuela, and Stork (2004) found better compliance with electronic diaries than with paper and pencil. On the other hand, Green, Rafaeli, Bolger, Shrout, & Reis (2006) demonstrated the psychometric data structure equivalence between these two methods, suggesting that the data collected in either method will yield similar statistical results given comparable compliance rates.

Daily diary/daily self-report and EMA measurement were somewhat rarely represented in this review, occurring in only 6.1% of the total studies. EMA methods had been used in only one of the reviewed studies. The recent proliferation of EMA and daily diary studies in psychology reported by others ( Bolger et al., 2003 ; Piasecki et al., 2007 ; Shiffman et al., 2008 ) suggests that these methods have not yet reached SCED researchers, which could in part have resulted from the long-held supremacy of observational measurement in fields that commonly practice single-case research.

Measurement Standards

As was previously mentioned, measurement in SCEDs requires the reliable assessment of change over time. As illustrated in Table 4 , DIV16 and the NRP explicitly require that reliability of all measures be reported. DIV12 provides little direction in the selection of the measurement instrument, except to require that three or more clinically important behaviors with relative independence be assessed. Similarly, the only item concerned with measurement on the Tate et al. scale specifies assessing behaviors consistent with the target of the intervention. The WWC and the Tate et al. scale require at least two independent assessors of the DV and that interrater reliability meeting minimum established thresholds be reported. Furthermore, WWC requires that interrater reliability be assessed on at least 20% of the data in each phase and in each condition. DIV16 expects that assessment of the outcome measures will be multisource and multimethod, when applicable. The interval of measurement is not specified by any of the reviewed sources. The WWC and the Tate et al. scale require that DVs be measured repeatedly across phases (e.g., baseline and treatment), which is a typical requirement of a SCED. The NRP asks that the time points at which DV measurement occurred be reported.

The baseline measurement represents one of the most crucial design elements of the SCED. Because subjects provide their own data for comparison, gathering a representative, stable sampling of behavior before manipulating the IV is essential to accurately inferring an effect. Some researchers have reported the typical length of the baseline period to range from 3 to 12 observations in intervention research applications (e.g., Center et al., 1986 ; Huitema, 1985 ; R. R. Jones et al., 1977 ; Sharpley, 1987 ); Huitema’s (1985) review of 881 experiments published in the Journal of Applied Behavior Analysis resulted in a modal number of three to four baseline points. Center et al. (1986) suggested five as the minimum number of baseline measurements needed to accurately estimate autocorrelation. Longer baseline periods suggest a greater likelihood of a representative measurement of the DVs, which has been found to increase the validity of the effects and reduce bias resulting from autocorrelation ( Huitema & McKean, 1994 ). The results of this review are largely consistent with those of previous researchers: The mean number of baseline observations was found to be 10.22 ( SD = 9.59), and 6 was the modal number of observations. Baseline data were available in 77.8% of the reviewed studies. Although the baseline assessment has tremendous bearing on the results of a SCED study, it was often difficult to locate the exact number of data points. Similarly, the number of data points assessed across all phases of the study were not easily identified.

The WWC, DIV12, and DIV16 agree that a minimum of three data points during the baseline is necessary. However, to receive the highest rating by the WWC, five data points are necessary in each phase, including the baseline and any subsequent withdrawal baselines as would occur in a reversal design. DIV16 explicitly states that more than three points are preferred and further stipulates that the baseline must demonstrate stability (i.e., limited variability), absence of overlap between the baseline and other phases, absence of a trend, and that the level of the baseline measurement is severe enough to warrant intervention; each of these aspects of the data is important in inferential accuracy. Detrending techniques can be used to address baseline data trend. The integration option in ARIMA-based modeling and the empirical mode decomposition method ( Wu, Huang, Long, & Peng, 2007 ) are two sophisticated detrending techniques. In regression-based analytic methods, detrending can be accomplished by simply regressing each variable in the model on time (i.e., the residuals become the detrended series), which is analogous to adding a linear, exponential, or quadratic term to the regression equation.

NRP does not provide a minimum for data points, nor does the Tate et al. scale, which requires only a sufficient sampling of baseline behavior. Although the mean and modal number of baseline observations is well within these parameters, seven (1.7%) studies reported mean baselines of less than three data points.

Establishing a uniform minimum number of required baseline observations would provide researchers and reviewers with only a starting guide. The baseline phase is important in SCED research because it establishes a trend that can then be compared with that of subsequent phases. Although a minimum number of observations might be required to meet standards, many more might be necessary to establish a trend when there is variability and trends in the direction of the expected effect. The selected data analytic approach also has some bearing on the number of necessary baseline observations. This is discussed further in the Analysis section.

Reporting of repeated measurements

Stone and Shiffman (2002) provide a comprehensive set of guidelines for the reporting of EMA data, which can also be applied to other repeated-measurement strategies. Because the application of EMA is widespread and not confined to specific research designs, Stone and Shiffman intentionally place few restraints on researchers regarding selection of the DV and the reporter, which is determined by the research question under investigation. The methods of measurement, however, are specified in detail: Descriptions of prompting, recording of responses, participant-initiated entries, and the data acquisition interface (e.g., paper and pencil diary, PDA, cellular telephone) ought to be provided with sufficient detail for replication. Because EMA specifically, and time-series/daily diary methods similarly, are primarily concerned with the interval of assessment, Stone and Shiffman suggest reporting the density and schedule of assessment. The approach is generally determined by the nature of the research question and pragmatic considerations, such as access to electronic data collection devices at certain times of the day and participant burden. Compliance and missing data concerns are present in any longitudinal research design, but they are of particular importance in repeated-measurement applications with frequent measurement. When the research question pertains to temporal effects, compliance becomes paramount, and timely, immediate responding is necessary. For this reason, compliance decisions, rates of missing data, and missing data management techniques must be reported. The effect of missing data in time-series data streams has been the topic of recent research in the social sciences (e.g., Smith, Borckardt, & Nash, in press ; Velicer & Colby, 2005a , 2005b ). The results and implications of these and other missing data studies are discussed in the next section.

Analysis of SCED Data

Visual analysis.

Experts in the field generally agree about the majority of critical single-case experiment design and measurement characteristics. Analysis, on the other hand, is an area of significant disagreement, yet it has also received extensive recent attention and advancement. Debate regarding the appropriateness and accuracy of various methods for analyzing SCED data, the interpretation of single-case effect sizes, and other concerns vital to the validity of SCED results has been ongoing for decades, and no clear consensus has been reached. Visual analysis, following systematic procedures such as those provided by Franklin, Gorman, Beasley, and Allison (1997) and Parsonson and Baer (1978) , remains the standard by which SCED data are most commonly analyzed ( Parker, Cryer, & Byrns, 2006 ). Visual analysis can arguably be applied to all SCEDs. However, a number of baseline data characteristics must be met for effects obtained through visual analysis to be valid and reliable. The baseline phase must be relatively stable; free of significant trend, particularly in the hypothesized direction of the effect; have minimal overlap of data with subsequent phases; and have a sufficient sampling of behavior to be considered representative ( Franklin, Gorman, et al., 1997 ; Parsonson & Baer, 1978 ). The effect of baseline trend on visual analysis, and a technique to control baseline trend, are offered by Parker et al. (2006) . Kazdin (2010) suggests using statistical analysis when a trend or significant variability appears in the baseline phase, two conditions that ought to preclude the use of visual analysis techniques. Visual analysis methods are especially adept at determining intervention effects and can be of particular relevance in real-world applications (e.g., Borckardt et al., 2008 ; Kratochwill, Levin, Horner, & Swoboda, 2011 ).

However, visual analysis has its detractors. It has been shown to be inconsistent, can be affected by autocorrelation, and results in overestimation of effect (e.g., Matyas & Greenwood, 1990 ). Visual analysis as a means of estimating an effect precludes the results of SCED research from being included in meta-analysis, and also makes it very difficult to compare results to the effect sizes generated by other statistical methods. Yet, visual analysis proliferates in large part because SCED researchers are familiar with these methods and are not only generally unfamiliar with statistical approaches, but lack agreement about their appropriateness. Still, top experts in single-case analysis champion the use of statistical methods alongside visual analysis whenever it is appropriate to do so ( Kratochwill et al., 2011 ).

Statistical analysis

Statistical analysis of SCED data consists generally of an attempt to address one or more of three broad research questions: (1) Does introduction/manipulation of the IV result in statistically significant change in the level of the DV (level-change or phase-effect analysis)? (2) Does introduction/manipulation of the IV result in statistically significant change in the slope of the DV over time (slope-change analysis)? and (3) Do meaningful relationships exist between the trajectory of the DV and other potential covariates? Level- and slope-change analyses are relevant to intervention effectiveness studies and other research questions in which the IV is expected to result in changes in the DV in a particular direction. Visual analysis methods are most adept at addressing research questions pertaining to changes in level and slope (Questions 1 and 2), most often using some form of graphical representation and standardized computation of a mean level or trend line within and between each phase of interest (e.g., Horner & Spaulding, 2010 ; Kratochwill et al., 2011 ; Matyas & Greenwood, 1990 ). Research questions in other areas of psychological science might address the relationship between DVs or the slopes of DVs (Question 3). A number of sophisticated modeling approaches (e.g., cross-lag, multilevel, panel, growth mixture, latent class analysis) may be used for this type of question, and some are discussed in greater detail later in this section. However, a discussion about the nuances of this type of analysis and all their possible methods is well beyond the scope of this article.

The statistical analysis of SCEDs is a contentious issue in the field. Not only is there no agreed-upon statistical method, but the practice of statistical analysis in the context of the SCED is viewed by some as unnecessary (see Shadish, Rindskopf, & Hedges, 2008 ). Traditional trends in the prevalence of statistical analysis usage by SCED researchers are revealing: Busk & Marascuilo (1992) found that only 10% of the published single-case studies they reviewed used statistical analysis; Brossart, Parker, Olson, & Mahadevan (2006) estimated that this figure had roughly doubled by 2006. A range of concerns regarding single-case effect size calculation and interpretation is discussed in significant detail elsewhere (e.g., Campbell, 2004 ; Cohen, 1994 ; Ferron & Sentovich, 2002 ; Ferron & Ware, 1995 ; Kirk, 1996 ; Manolov & Solanas, 2008 ; Olive & Smith, 2005 ; Parker & Brossart, 2003 ; Robey et al., 1999 ; Smith et al., in press ; Velicer & Fava, 2003 ). One concern is the lack of a clearly superior method across datasets. Although statistical methods for analyzing SCEDs abound, few studies have examined their comparative performance with the same dataset. The most recent studies of this kind, performed by Brossart et al. (2006) , Campbell (2004) , Parker and Brossart (2003) , and Parker and Vannest (2009) , found that the more promising available statistical analysis methods yielded moderately different results on the same data series, which led them to conclude that each available method is equipped to adequately address only a relatively narrow spectrum of data. Given these findings, analysts need to select an appropriate model for the research questions and data structure, being mindful of how modeling results can be influenced by extraneous factors.

The current standards unfortunately provide little guidance in the way of statistical analysis options. This article presents an admittedly cursory introduction to available statistical methods; many others are not covered in this review. The following articles provide more in-depth discussion and description of other methods: Barlow et al. (2008) ; Franklin et al., (1997) ; Kazdin (2010) ; and Kratochwill and Levin (1992 , 2010 ). Shadish et al. (2008) summarize more recently developed methods. Similarly, a Special Issue of Evidence-Based Communication Assessment and Intervention (2008, Volume 2) provides articles and discussion of the more promising statistical methods for SCED analysis. An introduction to autocorrelation and its implications for statistical analysis is necessary before specific analytic methods can be discussed. It is also pertinent at this time to discuss the implications of missing data.

Autocorrelation

Many repeated measurements within a single subject or unit create a situation that most psychological researchers are unaccustomed to dealing with: autocorrelated data, which is the nonindependence of sequential observations, also known as serial dependence. Basic and advanced discussions of autocorrelation in single-subject data can be found in Borckardt et al. (2008) , Huitema (1985) , and Marshall (1980) , and discussions of autocorrelation in multilevel models can be found in Snijders and Bosker (1999) and Diggle and Liang (2001) . Along with trend and seasonal variation, autocorrelation is one example of the internal structure of repeated measurements. In the social sciences, autocorrelated data occur most naturally in the fields of physiological psychology, econometrics, and finance, where each phase of interest has potentially hundreds or even thousands of observations that are tightly packed across time (e.g., electroencephalography actuarial data, financial market indices). Applied SCED research in most areas of psychology is more likely to have measurement intervals of day, week, or hour.

Autocorrelation is a direct result of the repeated-measurement requirements of the SCED, but its effect is most noticeable and problematic when one is attempting to analyze these data. Many commonly used data analytic approaches, such as analysis of variance, assume independence of observations and can produce spurious results when the data are nonindependent. Even statistically insignificant autocorrelation estimates are generally viewed as sufficient to cause inferential bias when conventional statistics are used (e.g., Busk & Marascuilo, 1988 ; R. R. Jones et al., 1977 ; Matyas & Greenwood, 1990 ). The effect of autocorrelation on statistical inference in single-case applications has also been known for quite some time (e.g., R. R. Jones et al., 1977 ; Kanfer, 1970 ; Kazdin, 1981 ; Marshall, 1980 ). The findings of recent simulation studies of single-subject data streams indicate that autocorrelation is a nontrivial matter. For example, Manolov and Solanas (2008) determined that calculated effect sizes were linearly related to the autocorrelation of the data stream, and Smith et al. (in press) demonstrated that autocorrelation estimates in the vicinity of 0.80 negatively affect the ability to correctly infer a significant level-change effect using a standardized mean differences method. Huitema and colleagues (e.g., Huitema, 1985 ; Huitema & McKean, 1994 ) argued that autocorrelation is rarely a concern in applied research. Huitema’s methods and conclusions have been questioned and opposing data have been published (e.g., Allison & Gorman, 1993 ; Matyas & Greenwood, 1990 ; Robey et al., 1999 ), resulting in abandonment of the position that autocorrelation can be conscionably ignored without compromising the validity of the statistical procedures. Procedures for removing autocorrelation in the data stream prior to calculating effect sizes are offered as one option: One of the more promising analysis methods, autoregressive integrated moving averages (discussed later in this article), was specifically designed to remove the internal structure of time-series data, such as autocorrelation, trend, and seasonality ( Box & Jenkins, 1970 ; Tiao & Box, 1981 ).

Missing observations

Another concern inherent in repeated-measures designs is missing data. Daily diary and EMA methods are intended to reduce the risk of retrospection error by eliciting accurate, real-time information ( Bolger et al., 2003 ). However, these methods are subject to missing data as a result of honest forgetfulness, not possessing the diary collection tool at the specified time of collection, and intentional or systematic noncompliance. With paper and pencil diaries and some electronic methods, subjects might be able to complete missed entries retrospectively, defeating the temporal benefits of these assessment strategies ( Bolger et al., 2003 ). Methods of managing noncompliance through the study design and measurement methods include training the subject to use the data collection device appropriately, using technology to prompt responding and track the time of response, and providing incentives to participants for timely compliance (for additional discussion of this topic, see Bolger et al., 2003 ; Shiffman & Stone, 1998 ).

Even when efforts are made to maximize compliance during the conduct of the research, the problem of missing data is often unavoidable. Numerous approaches exist for handling missing observations in group multivariate designs (e.g., Horton & Kleinman, 2007 ; Ibrahim, Chen, Lipsitz, & Herring, 2005 ). Ragunathan (2004) and others concluded that full information and raw data maximum likelihood methods are preferable. Velicer and Colby (2005a , 2005b ) established the superiority of maximum likelihood methods over listwise deletion, mean of adjacent observations, and series mean substitution in the estimation of various critical time-series data parameters. Smith et al. (in press) extended these findings regarding the effect of missing data on inferential precision. They found that managing missing data with the EM procedure ( Dempster, Laird, & Rubin, 1977 ), a maximum likelihood algorithm, did not affect one’s ability to correctly infer a significant effect. However, lag-1 autocorrelation estimates in the vicinity of 0.80 resulted in insufficient power sensitivity (< 0.80), regardless of the proportion of missing data (10%, 20%, 30%, or 40%). 1 Although maximum likelihood methods have garnered some empirical support, methodological strategies that minimize missing data, particularly systematically missing data, are paramount to post-hoc statistical remedies.

Nonnormal distribution of data

In addition to the autocorrelated nature of SCED data, typical measurement methods also present analytic challenges. Many statistical methods, particularly those involving model finding, assume that the data are normally distributed. This is often not satisfied in SCED research when measurements involve count data, observer-rated behaviors, and other, similar metrics that result in skewed distributions. Techniques are available to manage nonnormal distributions in regression-based analysis, such as zero-inflated Poisson regression ( D. Lambert, 1992 ) and negative binomial regression ( Gardner, Mulvey, & Shaw, 1995 ), but many other statistical analysis methods do not include these sophisticated techniques. A skewed data distribution is perhaps one of the reasons Kazdin (2010) suggests not using count, categorical, or ordinal measurement methods.

Available statistical analysis methods

Following is a basic introduction to the more promising and prevalent analytic methods for SCED research. Because there is little consensus regarding the superiority of any single method, the burden unfortunately falls on the researcher to select a method capable of addressing the research question and handling the data involved in the study. Some indications and contraindications are provided for each method presented here.

Multilevel and structural equation modeling

Multilevel modeling (MLM; e.g., Schmidt, Perels, & Schmitz, 2010 ) techniques represent the state of the art among parametric approaches to SCED analysis, particularly when synthesizing SCED results ( Shadish et al., 2008 ). MLM and related latent growth curve and factor mixture methods in structural equation modeling (SEM; e.g., Lubke & Muthén, 2005 ; B. O. Muthén & Curran, 1997 ) are particularly effective for evaluating trajectories and slopes in longitudinal data and relating changes to potential covariates. MLM and related hierarchical linear models (HLM) can also illuminate the relationship between the trajectories of different variables under investigation and clarify whether or not these relationships differ amongst the subjects in the study. Time-series and cross-lag analyses can also be used in MLM and SEM ( Chow, Ho, Hamaker, & Dolan, 2010 ; du Toit & Browne, 2007 ). However, they generally require sophisticated model-fitting techniques, making them difficult for many social scientists to implement. The structure (autocorrelation) and trend of the data can also complicate many MLM methods. The common, short data streams in SCED research and the small number of subjects also present problems to MLM and SEM approaches, which were developed for data with significantly greater numbers of observations when the number of subjects is fewer, and for a greater number of participants for model-fitting purposes, particularly when there are fewer data points. Still, MLM and related techniques arguably represent the most promising analytic methods.

A number of software options 2 exist for SEM. Popular statistical packages in the social sciences provide SEM options, such as PROC CALIS in SAS ( SAS Institute Inc., 2008 ), the AMOS module ( Arbuckle, 2006 ) of SPSS ( SPSS Statistics, 2011 ), and the sempackage for R ( R Development Core Team, 2005 ), the use of which is described by Fox ( Fox, 2006 ). A number of stand-alone software options are also available for SEM applications, including Mplus ( L. K. Muthén & Muthén, 2010 ) and Stata ( StataCorp., 2011 ). Each of these programs also provides options for estimating multilevel/hierarchical models (for a review of using these programs for MLM analysis see Albright & Marinova, 2010 ). Hierarchical linear and nonlinear modeling can also be accomplished using the HLM 7 program ( Raudenbush, Bryk, & Congdon, 2011 ).

Autoregressive moving averages (ARMA; e.g., Browne & Nesselroade, 2005 ; Liu & Hudack, 1995 ; Tiao & Box, 1981 )

Two primary points have been raised regarding ARMA modeling: length of the data stream and feasibility of the modeling technique. ARMA models generally require 30–50 observations in each phase when analyzing a single-subject experiment (e.g., Borckardt et al., 2008 ; Box & Jenkins, 1970 ), which is often difficult to satisfy in applied psychological research applications. However, ARMA models in an SEM framework, such as those described by du Toit & Browne (2001) , are well suited for longitudinal panel data with few observations and many subjects. Autoregressive SEM models are also applicable under similar conditions. Model-fitting options are available in SPSS, R, and SAS via PROC ARMA.

ARMA modeling also requires considerable training in the method and rather advanced knowledge about statistical methods (e.g., Kratochwill & Levin, 1992 ). However, Brossart et al. (2006) point out that ARMA-based approaches can produce excellent results when there is no “model finding” and a simple lag-1 model, with no differencing and no moving average, is used. This approach can be taken for many SCED applications when phase- or slope-change analyses are of interest with a single, or very few, subjects. As already mentioned, this method is particularly useful when one is seeking to account for autocorrelation or other over-time variations that are not directly related to the experimental or intervention effect of interest (i.e., detrending). ARMA and other time-series analysis methods require missing data to be managed prior to analysis by means of options such as full information maximum likelihood estimation, multiple imputation, or the Kalman filter (see Box & Jenkins, 1970 ; Hamilton, 1994 ; Shumway & Stoffer, 1982 ) because listwise deletion has been shown to result in inaccurate time-series parameter estimates ( Velicer & Colby, 2005a ).

Standardized mean differences

Standardized mean differences approaches include the common Cohen’s d , Glass’s Delta, and Hedge’s g that are used in the analysis of group designs. The computational properties of mean differences approaches to SCEDs are identical to those used for group comparisons, except that the results represent within-case variation instead of the variation between groups, which suggests that the obtained effect sizes are not interpretively equivalent. The advantage of the mean differences approach is its simplicity of calculation and also its familiarity to social scientists. The primary drawback of these approaches is that they were not developed to contend with autocorrelated data. However, Manolov and Solanas (2008) reported that autocorrelation least affected effect sizes calculated using standardized mean differences approaches. To the applied-research scientist this likely represents the most accessible analytic approach, because statistical software is not required to calculate these effect sizes. The resultant effect sizes of single subject standardized mean differences analysis must be interpreted cautiously because their relation to standard effect size benchmarks, such as those provided by Cohen (1988) , is unknown. Standardized mean differences approaches are appropriate only when examining significant differences between phases of the study and cannot illuminate trajectories or relationships between variables.

Other analytic approaches

Researchers have offered other analytic methods to deal with the characteristics of SCED data. A number of methods for analyzing N -of-1 experiments have been developed. Borckardt’s Simulation Modeling Analysis (2006) program provides a method for analyzing level- and slope-change in short (<30 observations per phase; see Borckardt et al., 2008 ), autocorrelated data streams that is statistically sophisticated, yet accessible and freely available to typical psychological scientists and clinicians. A replicated single-case time-series design conducted by Smith, Handler, & Nash (2010) provides an example of SMA application. The Singwin Package, described in Bloom et al., (2003) , is a another easy-to-use parametric approach for analyzing single-case experiments. A number of nonparametric approaches have also been developed that emerged from the visual analysis tradition: Some examples include percent nonoverlapping data ( Scruggs, Mastropieri, & Casto, 1987 ) and nonoverlap of all pairs ( Parker & Vannest, 2009 ); however, these methods have come under scrutiny, and Wolery, Busick, Reichow, and Barton (2010) have suggested abandoning them altogether. Each of these methods appears to be well suited for managing specific data characteristics, but they should not be used to analyze data streams beyond their intended purpose until additional empirical research is conducted.

Combining SCED Results

Beyond the issue of single-case analysis is the matter of integrating and meta-analyzing the results of single-case experiments. SCEDs have been given short shrift in the majority of meta-analytic literature ( Littell, Corcoran, & Pillai, 2008 ; Shadish et al., 2008 ), with only a few exceptions ( Carr et al., 1999 ; Horner & Spaulding, 2010 ). Currently, few proven methods exist for integrating the results of multiple single-case experiments. Allison and Gorman (1993) and Shadish et al. (2008) present the problems associated with meta-analyzing single-case effect sizes, and W. P. Jones (2003) , Manolov and Solanas (2008) , Scruggs and Mastropieri (1998) , and Shadish et al. (2008) offer four different potential statistical solutions for this problem, none of which appear to have received consensus amongst researchers. The ability to synthesize and compare single-case effect sizes, particularly effect sizes garnered through group design research, is undoubtedly necessary to increase SCED proliferation.

Discussion of Review Results and Coding of Analytic Methods

The coding criteria for this review were quite stringent in terms of what was considered to be either visual or statistical analysis. For visual analysis to be coded as present, it was necessary for the authors to self-identify as having used a visual analysis method. In many cases, it could likely be inferred that visual analysis had been used, but it was often not specified. Similarly, statistical analysis was reserved for analytic methods that produced an effect. 3 Analyses that involved comparing magnitude of change using raw count data or percentages were not considered rigorous enough. These two narrow definitions of visual and statistical analysis contributed to the high rate of unreported analytic method, shown in Table 1 (52.3%). A better representation of the use of visual and statistical analysis would likely be the percentage of studies within those that reported a method of analysis. Under these parameters, 41.5% used visual analysis and 31.3% used statistical analysis. Included in these figures are studies that included both visual and statistical methods (11%). These findings are slightly higher than those estimated by Brossart et al. (2006) , who estimated statistical analysis is used in about 20% of SCED studies. Visual analysis continues to undoubtedly be the most prevalent method, but there appears to be a trend for increased use of statistical approaches, which is likely to only gain momentum as innovations continue.

Analysis Standards

The standards selected for inclusion in this review offer minimal direction in the way of analyzing the results of SCED research. Table 5 summarizes analysis-related information provided by the six reviewed sources for SCED standards. Visual analysis is acceptable to DV12 and DIV16, along with unspecified statistical approaches. In the WWC standards, visual analysis is the acceptable method of determining an intervention effect, with statistical analyses and randomization tests permissible as a complementary or supporting method to the results of visual analysis methods. However, the authors of the WWC standards state, “As the field reaches greater consensus about appropriate statistical analyses and quantitative effect-size measures, new standards for effect demonstration will need to be developed” ( Kratochwill et al., 2010 , p.16). The NRP and DIV12 seem to prefer statistical methods when they are warranted. The Tate at al. scale accepts only statistical analysis with the reporting of an effect size. Only the WWC and DIV16 provide guidance in the use of statistical analysis procedures: The WWC “recommends” nonparametric and parametric approaches, multilevel modeling, and regression when statistical analysis is used. DIV16 refers the reader to Wilkinson and the Task Force on Statistical Inference of the APA Board of Scientific Affairs (1999) for direction in this matter. Statistical analysis of daily diary and EMA methods is similarly unsettled. Stone and Shiffman (2002) ask for a detailed description of the statistical procedures used, in order for the approach to be replicated and evaluated. They provide direction for analyzing aggregated and disaggregated data. They also aptly note that because many different modes of analysis exist, researchers must carefully match the analytic approach to the hypotheses being pursued.

Limitations and Future Directions

This review has a number of limitations that leave the door open for future study of SCED methodology. Publication bias is a concern in any systematic review. This is particularly true for this review because the search was limited to articles published in peer-reviewed journals. This strategy was chosen in order to inform changes in the practice of reporting and of reviewing, but it also is likely to have inflated the findings regarding the methodological rigor of the reviewed works. Inclusion of book chapters, unpublished studies, and dissertations would likely have yielded somewhat different results.

A second concern is the stringent coding criteria in regard to the analytic methods and the broad categorization into visual and statistical analytic approaches. The selection of an appropriate method for analyzing SCED data is perhaps the murkiest area of this type of research. Future reviews that evaluate the appropriateness of selected analytic strategies and provide specific decision-making guidelines for researchers would be a very useful contribution to the literature. Although six sources of standards apply to SCED research reviewed in this article, five of them were developed almost exclusively to inform psychological and behavioral intervention research. The principles of SCED research remain the same in different contexts, but there is a need for non–intervention scientists to weigh in on these standards.

Finally, this article provides a first step in the synthesis of the available SCED reporting guidelines. However, it does not resolve disagreements, nor does it purport to be a definitive source. In the future, an entity with the authority to construct such a document ought to convene and establish a foundational, adaptable, and agreed-upon set of guidelines that cuts across subspecialties but is applicable to many, if not all, areas of psychological research, which is perhaps an idealistic goal. Certain preferences will undoubtedly continue to dictate what constitutes acceptable practice in each subspecialty of psychology, but uniformity along critical dimensions will help advance SCED research.

Conclusions

The first decade of the twenty-first century has seen an upwelling of SCED research across nearly all areas of psychology. This article contributes updated benchmarks in terms of the frequency with which SCED design and methodology characteristics are used, including the number of baseline observations, assessment and measurement practices, and data analytic approaches, most of which are largely consistent with previously reported benchmarks. However, this review is much broader than those of previous research teams and also breaks down the characteristics of single-case research by the predominant design. With the recent SCED proliferation came a number of standards for the conduct and reporting of such research. This article also provides a much-needed synthesis of recent SCED standards that can inform the work of researchers, reviewers, and funding agencies conducting and evaluating single-case research, which reveals many areas of consensus as well as areas of significant disagreement. It appears that the question of where to go next is very relevant at this point in time. The majority of the research design and measurement characteristics of the SCED are reasonably well established, and the results of this review suggest general practice that is in accord with existing standards and guidelines, at least in regard to published peer-reviewed works. In general, the published literature appears to be meeting the basic design and measurement requirement to ensure adequate internal validity of SCED studies.

Consensus regarding the superiority of any one analytic method stands out as an area of divergence. Judging by the current literature and lack of consensus, researchers will need to carefully select a method that matches the research design, hypotheses, and intended conclusions of the study, while also considering the most up-to-date empirical support for the chosen analytic method, whether it be visual or statistical. In some cases the number of observations and subjects in the study will dictate which analytic methods can and cannot be used. In the case of the true N -of-1 experiment, there are relatively few sound analytic methods, and even fewer that are robust with shorter data streams (see Borckardt et al., 2008 ). As the number of observations and subjects increases, sophisticated modeling techniques, such as MLM, SEM, and ARMA, become applicable. Trends in the data and autocorrelation further obfuscate the development of a clear statistical analysis selection algorithm, which currently does not exist. Autocorrelation was rarely addressed or discussed in the articles reviewed, except when the selected statistical analysis dictated consideration. Given the empirical evidence regarding the effect of autocorrelation on visual and statistical analysis, researchers need to address this more explicitly. Missing-data considerations are similarly left out when they are unnecessary for analytic purposes. As newly devised statistical analysis approaches mature and are compared with one another for appropriateness in specific SCED applications, guidelines for statistical analysis will necessarily be revised. Similarly, empirically derived guidance, in the form of a decision tree, must be developed to ensure application of appropriate methods based on characteristics of the data and the research questions being addressed. Researchers could also benefit from tutorials and comparative reviews of different software packages: This is a needed area of future research. Powerful and reliable statistical analyses help move the SCED up the ladder of experimental designs and attenuate the view that the method applies primarily to pilot studies and idiosyncratic research questions and situations.

Another potential future advancement of SCED research comes in the area of measurement. Currently, SCED research gives significant weight to observer ratings and seems to discourage other forms of data collection methods. This is likely due to the origins of the SCED in behavioral assessment and applied behavior analysis, which remains a present-day stronghold. The dearth of EMA and diary-like sampling procedures within the SCED research reviewed, yet their ever-growing prevalence in the larger psychological research arena, highlights an area for potential expansion. Observational measurement, although reliable and valid in many contexts, is time and resource intensive and not feasible in all areas in which psychologists conduct research. It seems that numerous untapped research questions are stifled because of this measurement constraint. SCED researchers developing updated standards in the future should include guidelines for the appropriate measurement requirement of non-observer-reported data. For example, the results of this review indicate that reporting of repeated measurements, particularly the high-density type found in diary and EMA sampling strategies, ought to be more clearly spelled out, with specific attention paid to autocorrelation and trend in the data streams. In the event that SCED researchers adopt self-reported assessment strategies as viable alternatives to observation, a set of standards explicitly identifying the necessary psychometric properties of the measures and specific items used would be in order.

Along similar lines, SCED researchers could take a page from other areas of psychology that champion multimethod and multisource evaluation of primary outcomes. In this way, the long-standing tradition of observational assessment and the cutting-edge technological methods of EMA and daily diary could be married with the goal of strengthening conclusions drawn from SCED research and enhancing the validity of self-reported outcome assessment. The results of this review indicate that they rarely intersect today, and I urge SCED researchers to adopt other methods of assessment informed by time-series, daily diary, and EMA methods. The EMA standards could serve as a jumping-off point for refined measurement and assessment reporting standards in the context of multimethod SCED research.

One limitation of the current SCED standards is their relatively limited scope. To clarify, with the exception of the Stone & Shiffman EMA reporting guidelines, the other five sources of standards were developed in the context of designing and evaluating intervention research. Although this is likely to remain its patent emphasis, SCEDs are capable of addressing other pertinent research questions in the psychological sciences, and the current standards truly only roughly approximate salient crosscutting SCED characteristics. I propose developing broad SCED guidelines that address the specific design, measurement, and analysis issues in a manner that allows it to be useful across applications, as opposed to focusing solely on intervention effects. To accomplish this task, methodology experts across subspecialties in psychology would need to convene. Admittedly this is no small task.

Perhaps funding agencies will also recognize the fiscal and practical advantages of SCED research in certain areas of psychology. One example is in the field of intervention effectiveness, efficacy, and implementation research. A few exemplary studies using robust forms of SCED methodology are needed in the literature. Case-based methodologies will never supplant the group design as the gold standard in experimental applications, nor should that be the goal. Instead, SCEDs provide a viable and valid alternative experimental methodology that could stimulate new areas of research and answer questions that group designs cannot. With the astonishing number of studies emerging every year that use single-case designs and explore the methodological aspects of the design, we are poised to witness and be a part of an upsurge in the sophisticated application of the SCED. When federal grant-awarding agencies and journal editors begin to use formal standards while making funding and publication decisions, the field will benefit.

Last, for the practice of SCED research to continue and mature, graduate training programs must provide students with instruction in all areas of the SCED. This is particularly true of statistical analysis techniques that are not often taught in departments of psychology and education, where the vast majority of SCED studies seem to be conducted. It is quite the conundrum that the best available statistical analytic methods are often cited as being inaccessible to social science researchers who conduct this type of research. This need not be the case. To move the field forward, emerging scientists must be able to apply the most state-of-the-art research designs, measurement techniques, and analytic methods.

Acknowledgments

Research support for the author was provided by research training grant MH20012 from the National Institute of Mental Health, awarded to Elizabeth A. Stormshak. The author gratefully acknowledges Robert Horner and Laura Lee McIntyre, University of Oregon; Michael Nash, University of Tennessee; John Ferron, University of South Florida; the Action Editor, Lisa Harlow, and the anonymous reviewers for their thoughtful suggestions and guidance in shaping this article; Cheryl Mikkola for her editorial support; and Victoria Mollison for her assistance in the systematic review process.

Appendix. Results of Systematic Review Search and Studies Included in the Review

Psycinfo search conducted july 2011.

• Alternating treatment design
• Changing criterion design
• Experimental case*
• Multiple baseline design
• Replicated single-case design
• Simultaneous treatment design
• Time-series design
• Quantitative study OR treatment outcome/randomized clinical trial
• NOT field study OR interview OR focus group OR literature review OR systematic review OR mathematical model OR qualitative study
• Publication range: 2000–2010
• Published in peer-reviewed journals
• Available in the English Language

Bibliography

(* indicates inclusion in study: N = 409)

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2 The author makes no endorsement regarding the superiority of any statistical program or package over another by their mention or exclusion in this article. The author also has no conflicts of interest in this regard.

3 However, it should be noted that it was often very difficult to locate an actual effect size reported in studies that used statistical analysis. Although this issue would likely have added little to this review, it does inhibit the inclusion of the results in meta-analysis.

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10.2 Single-Subject Research Designs

Learning objectives.

• Describe the basic elements of a single-subject research design.
• 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.

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 10.3 “Results of a Generic Single-Subject Study Illustrating Several Principles of Single-Subject Research” , 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 10.3 “Results of a Generic Single-Subject Study Illustrating Several Principles of Single-Subject Research” 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 10.3 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. There may be a period of adjustment to the treatment during which the behavior of interest becomes more variable and begins to increase or decrease. 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 10.4 “An Approximation of the Results for Hall and Colleagues’ Participant Robbie in Their ABAB Reversal Design” approximates the data for Robbie. 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 10.4 An Approximation of the Results for Hall and Colleagues’ Participant Robbie in Their ABAB Reversal Design

Why is the reversal—the removal of the treatment—considered to be necessary in this type of design? Why use an ABA design, for example, rather than a simpler AB design? Notice that an AB design is essentially an interrupted time-series design applied to an individual participant. Recall that one problem with that design is that 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.

There are close relatives of the basic reversal design that allow for the evaluation of more than one treatment. In a multiple-treatment reversal design , a baseline phase is followed by separate phases in which different treatments are introduced. For example, a researcher might establish a baseline of studying behavior for a disruptive student (A), then introduce a treatment involving positive attention from the teacher (B), and then switch to a treatment involving mild punishment for not studying (C). The participant could then be returned to a baseline phase before reintroducing each treatment—perhaps in the reverse order as a way of controlling for carryover effects. This particular multiple-treatment reversal design could also be referred to as an ABCACB design.

In an alternating treatments design , two or more treatments are alternated relatively quickly on a regular schedule. For example, positive attention for studying could be used one day and mild punishment for not studying the next, and so on. Or one treatment could be implemented in the morning and another in the afternoon. The alternating treatments design can be a quick and effective way of comparing treatments, but only when the treatments are fast acting.

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. Perhaps something else happened at about the same time as the treatment—for example, the student’s parents might have started rewarding him for good grades.

One solution to these problems is to use a multiple-baseline design , which is represented in Figure 10.5 “Results of a Generic Multiple-Baseline Study” . 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 extremely unlikely to be a coincidence.

Figure 10.5 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 & Horner, 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—a very unlikely occurrence—to explain their results.

In another version of the multiple-baseline design, multiple baselines are established for the same participant but for different dependent variables, and the treatment is introduced at a different time for each dependent variable. Imagine, for example, a study on the effect of setting clear goals on the productivity of an office worker who has two primary tasks: making sales calls and writing reports. Baselines for both tasks could be established. For example, the researcher could measure the number of sales calls made and reports written by the worker each week for several weeks. Then the goal-setting treatment could be introduced for one of these tasks, and at a later time the same treatment could be introduced for the other task. The logic is the same as before. If productivity increases on one task after the treatment is introduced, it is unclear whether the treatment caused the increase. But if productivity increases on both tasks after the treatment is introduced—especially when the treatment is introduced at two different times—then it seems much clearer that the treatment was responsible.

In yet a third version of the multiple-baseline design, multiple baselines are established for the same participant but in different settings. For example, a baseline might be established for the amount of time a child spends reading during his free time at school and during his free time at home. Then a treatment such as positive attention might be introduced first at school and later at home. Again, if the dependent variable changes after the treatment is introduced in each setting, then this gives the researcher confidence that the treatment is, in fact, responsible for the change.

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. Group data are described using statistics such as means, standard deviations, Pearson’s r , and so on to detect general patterns. Finally, 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 10.6 , 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 10.6 , 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 10.6

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, 2001). 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.

Key Takeaways

• 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.
• In a reversal design, the participant is tested in a baseline condition, then tested in a treatment condition, and then returned to baseline. If the dependent variable changes with the introduction of the treatment and then changes back with the return to baseline, this provides strong evidence of a treatment effect.
• In a multiple-baseline design, baselines are established for different participants, different dependent variables, or different settings—and the treatment is introduced at a different time on each baseline. If the introduction of the treatment is followed by a change in the dependent variable on each baseline, this provides strong evidence of a treatment effect.
• 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.

Practice: Design a simple single-subject study (using either a reversal or multiple-baseline design) to answer the following questions. Be sure to specify the treatment, operationally define the dependent variable, decide when and where the observations will be made, and so on.

• 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.

Fisch, G. S. (2001). Evaluating data from behavioral analysis: Visual inspection or statistical models. Behavioural Processes , 54 , 137–154.

Ross, S. W., & Horner, R. H. (2009). Bully prevention in positive behavior support. Journal of Applied Behavior Analysis , 42 , 747–759.

Scruggs, T. E., & Mastropieri, M. A. (2001). How to summarize single-participant research: Ideas and applications. Exceptionality , 9 , 227–244.

Sidman, M. (1960). Tactics of scientific research: Evaluating experimental data in psychology . Boston, MA: Authors Cooperative.

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

10.1 Overview of Single-Subject Research

Learning objectives.

• Explain what single-subject research is, including how it differs from other types of psychological research.
• Explain who uses single-subject research and why.

What Is Single-Subject Research?

Single-subject research  is a type of quantitative 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 textbook 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 more applied areas of psychology.

Before continuing, it is important to distinguish single-subject research from case studies and other more qualitative approaches that involve studying in detail a small number of participants. As described in Chapter 6, case studies involve an in-depth analysis and description of an individual, which is typically primarily qualitative in nature. More broadly speaking, qualitative research focuses on understanding people’s subjective experience by observing behavior and collecting relatively unstructured data (e.g., detailed interviews) and analyzing those data using narrative rather than quantitative techniques. Single-subject research, in contrast, focuses on understanding objective behavior through experimental manipulation and control, collecting highly structured data, and analyzing those data quantitatively.

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 several 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.

A second assumption of single-subject research is that it is important to discover causal relationships through the manipulation of an independent variable, the careful measurement of a dependent variable, and the control of extraneous variables. For this reason, single-subject research is often considered a type of experimental research with good internal validity. Recall, for example, that Hall and his colleagues measured their dependent variable (studying) many times—first under a no-treatment control condition, then under a treatment condition (positive teacher attention), and then again under the control condition. Because there was a clear increase in studying when the treatment was introduced, a decrease when it was removed, and an increase when it was reintroduced, there is little doubt that the treatment was the cause of the improvement.

A third 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, 1976) [1] . 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) [2] . 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 excellent 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, Wolf, & Risley, 1968) [3] . Applied behavior analysis plays an especially important role in contemporary research on developmental disabilities, education, organizational behavior, and health, among many other areas. Excellent examples of this work (including the study by Hall and his colleagues) can be found in the  Journal of Applied Behavior Analysis .

Although most contemporary single-subject research is conducted from the behavioral perspective, it can in principle be used to address questions framed in terms of any theoretical perspective. For example, a studying technique based on cognitive principles of learning and memory could be evaluated by testing it on individual high school students using the single-subject approach. 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, 1982) [4] .

Key Takeaways

• 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 qualitative research on a single person or small number of individuals. Unlike more qualitative research, single-subject research focuses on understanding objective behavior through experimental manipulation and control, collecting highly structured data, and analyzing those data quantitatively.
• Single-subject research has been around since the beginning of the field of psychology. Today it is most strongly associated with the behavioral theoretical perspective, but it can in principle be used to study behavior from any perspective.
• Practice: Find and read a published article in psychology that reports new single-subject research. (An archive of articles published in the Journal of Applied Behavior Analysis can be found at http://www.ncbi.nlm.nih.gov/pmc/journals/309/ ) Write a short summary of the study.
• Wolf, M. (1976). Social validity: The case for subjective measurement or how applied behavior analysis is finding its heart.  Journal of Applied Behavior Analysis, 11 , 203–214. ↵
• Skinner, B. F. (1938). T he behavior of organisms: An experimental analysis . New York, NY: Appleton-Century-Crofts. ↵
• Baer, D. M., Wolf, M. M., & Risley, T. R. (1968). Some current dimensions of applied behavior analysis.  Journal of Applied Behavior Analysis, 1 , 91–97. ↵
• Kazdin, A. E. (1982).  Single-case research designs: Methods for clinical and applied settings . New York, NY: Oxford University Press. ↵

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Educational Research Basics by Del Siegle

Single subject research.

“ Single subject research (also known as single case experiments) is popular in the fields of special education and counseling. This research design is useful when the researcher is attempting to change the behavior of an individual or a small group of individuals and wishes to document that change. Unlike true experiments where the researcher randomly assigns participants to a control and treatment group, in single subject research the participant serves as both the control and treatment group. The researcher uses line graphs to show the effects of a particular intervention or treatment.  An important factor of single subject research is that only one variable is changed at a time. Single subject research designs are “weak when it comes to external validity….Studies involving single-subject designs that show a particular treatment to be effective in changing behavior must rely on replication–across individuals rather than groups–if such results are be found worthy of generalization” (Fraenkel & Wallen, 2006, p. 318).

Suppose a researcher wished to investigate the effect of praise on reducing disruptive behavior over many days. First she would need to establish a baseline of how frequently the disruptions occurred. She would measure how many disruptions occurred each day for several days. In the example below, the target student was disruptive seven times on the first day, six times on the second day, and seven times on the third day. Note how the sequence of time is depicted on the x-axis (horizontal axis) and the dependent variable (outcome variable) is depicted on the y-axis (vertical axis).

Once a baseline of behavior has been established (when a consistent pattern emerges with at least three data points), the intervention begins. The researcher continues to plot the frequency of behavior while implementing the intervention of praise.

In this example, we can see that the frequency of disruptions decreased once praise began. The design in this example is known as an A-B design. The baseline period is referred to as A and the intervention period is identified as B.

Another design is the A-B-A design. An A-B-A design (also known as a reversal design) involves discontinuing the intervention and returning to a nontreatment condition.

Sometimes an individual’s behavior is so severe that the researcher cannot wait to establish a baseline and must begin with an intervention. In this case, a B-A-B design is used. The intervention is implemented immediately (before establishing a baseline). This is followed by a measurement without the intervention and then a repeat of the intervention.

Multiple-Baseline Design

Sometimes, a researcher may be interested in addressing several issues for one student or a single issue for several students. In this case, a multiple-baseline design is used.

“In a multiple baseline across subjects design, the researcher introduces the intervention to different persons at different times. The significance of this is that if a behavior changes only after the intervention is presented, and this behavior change is seen successively in each subject’s data, the effects can more likely be credited to the intervention itself as opposed to other variables. Multiple-baseline designs do not require the intervention to be withdrawn. Instead, each subject’s own data are compared between intervention and nonintervention behaviors, resulting in each subject acting as his or her own control (Kazdin, 1982). An added benefit of this design, and all single-case designs, is the immediacy of the data. Instead of waiting until postintervention to take measures on the behavior, single-case research prescribes continuous data collection and visual monitoring of that data displayed graphically, allowing for immediate instructional decision-making. Students, therefore, do not linger in an intervention that is not working for them, making the graphic display of single-case research combined with differentiated instruction responsive to the needs of students.” (Geisler, Hessler, Gardner, & Lovelace, 2009)

Regardless of the research design, the line graphs used to illustrate the data contain a set of common elements.

Generally, in single subject research we count the number of times something occurs in a given time period and see if it occurs more or less often in that time period after implementing an intervention. For example, we might measure how many baskets someone makes while shooting for 2 minutes. We would repeat that at least three times to get our baseline. Next, we would test some intervention. We might play music while shooting, give encouragement while shooting, or video the person while shooting to see if our intervention influenced the number of shots made. After the 3 baseline measurements (3 sets of 2 minute shooting), we would measure several more times (sets of 2 minute shooting) after the intervention and plot the time points (number of baskets made in 2 minutes for each of the measured time points). This works well for behaviors that are distinct and can be counted.

Sometimes behaviors come and go over time (such as being off task in a classroom or not listening during a coaching session). The way we can record these is to select a period of time (say 5 minutes) and mark down every 10 seconds whether our participant is on task. We make a minimum of three sets of 5 minute observations for a baseline, implement an intervention, and then make more sets of 5 minute observations with the intervention in place. We use this method rather than counting how many times someone is off task because one could continually be off task and that would only be a count of 1 since the person was continually off task. Someone who might be off task twice for 15 second would be off task twice for a score of 2. However, the second person is certainly not off task twice as much as the first person. Therefore, recording whether the person is off task at 10-second intervals gives a more accurate picture. The person continually off task would have a score of 30 (off task at every second interval for 5 minutes) and the person off task twice for a short time would have a score of 2 (off task only during 2 of the 10 second interval measures.

I also have additional information about how to record single-subject research data .

I hope this helps you better understand single subject research.

I have created a PowerPoint on Single Subject Research , which also available below as a video.

I have also created instructions for creating single-subject research design graphs with Excel .

Fraenkel, J. R., & Wallen, N. E. (2006). How to design and evaluate research in education (6th ed.). Boston, MA: McGraw Hill.

Geisler, J. L., Hessler, T., Gardner, R., III, & Lovelace, T. S. (2009). Differentiated writing interventions for high-achieving urban African American elementary students. Journal of Advanced Academics, 20, 214–247.

Del Siegle, Ph.D. University of Connecticut [email protected] www.delsiegle.info

Revised 02/02/2024

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D-3: Identify defining features of single-subject experimental designs (e.g., individuals serve as their own controls, repeated measures, prediction, verification, replication)©

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Target terms (or phrases, in this case): Individuals serve as their own controls, repeated measures, prediction, verification, control

Two important things to know about single subject experimental designs: (1) They are not the same as case studies. Case studies are clinical stories that just tell what happened without manipulation of the environment. Experimental designs involve deliberate manipulation of the environment to answer a particular question. (2) The logic behind single subject experimental designs applies to the everyday work of programming for behavior change with clients. Even if we never publish a research study in a peer reviewed journal, or participate in any kind of formal research, we still need to be very familiar with the methodology in order to evaluate our work as behavior analysts. This is not optional – it’s an integral part of our work.

Individuals serve as their own controls

Please note that “subject” and “participant” are two words that can be used to describe someone (or a unit of people or animals) in a research study. “Participant” is often a preferred term because it emphasizes that people who take part in studies have rights and are actively part of the process. 

Definition: Individuals serve as their own controls in a research study when the effects of an intervention are measured on the person themselves, not between one person who got the intervention (treatment) and one person who didn’t (control). In single subject methodology, the individual is essentially assigned to both treatment and control, because the research question is answered differently from other kinds of research. (See D-4 for more about what this all means.)

Example in clinical context: Tami is designing an intervention for her client Ariel, who needs help with remembering to complete her homework. Tami takes baseline data until stability is achieved, then introduces an intervention (series of alarms on Ariel’s phone) and continues to take data until stability is once again achieved. She then returns Ariel to the baseline condition and then introduces the intervention a second time, following the same process as before. The data depicting the dependent variable (Ariel’s homework completion behavior) show a clear relationship between the presence of the alarms and the completion of homework. In this example, no other person was used as a “control” for Ariel. That would not have been a great way to answer the question about how to help Ariel do her homework, since she might have special considerations and circumstances that are unique. Instead, she was the only subject, and the intervention was evaluated using Ariel herself in all phases. 

Why it matters: Using subjects as their own controls matters a lot in behavior analysis. It enables us to take into account the unique idiosyncrasies (“weirdness”) of each individual person. We’re all different, and we’re all weird in some way. When we use big groups to answer research questions, one of the goals is to make the groups so big that the numbers “drown out” the differences between people by statistically canceling each other out. There’s nothing inherently wrong with this, but it doesn’t work for us as behavior analysts. We are interested in functional relations between individual behavior and experimental conditions! To do that, we need to study the individual and their environment, and how the two interact. The vast majority of research published in behavior analytic journals was conducted using single subject methodology. 

Repeated measures

Definition: When we use single subject experimental designs, we need to capture something to measure to see if our intervention is working. That thing we measure is called a dependent variable. 

Examples in clinical context: Randi engages in swearing and property destruction. His team creates an intervention plan for him. In order to empirically answer questions about whether the intervention is working, the team carefully defines and records instances of Randi’s target behaviors. 

This also works with skill acquisition (behavior we are teaching so that they will increase). For example, say your client Tanisha needs more skills related to asking for help. We could use “asking for help” as the dependent variable and measure it multiple times throughout the baseline and intervention. 

Why it matters: Using repeated measures is super important, because if we only measure the dependent variable once or twice, we won’t be able to thoroughly see what our data points are telling us. Take a look at C-11 (interpret graph data) to understand more about how repeated measures help us analyze level, trend, and variability of data. 

Definition: Prediction is looking at the data we have and making an informed guess about where it would go if we kept all variables the same (i.e. if we didn’t change anything). Take a look at C-11 (interpret graph data) for more on how to predict where data will head next. 

Example in clinical context: Johnny is a client who is being assessed at a severe behavior clinic due to self injury. His team conducts observations and they highly suspect that his self injury is maintained by access to attention (connection with other people). The team conducts a functional assessment (baseline) condition in which they give Johnny attention every time his self injury occurs. Team members observe that Johnny engages in self injury every single time attention is withdrawn, and stops once he receives attention. After observing this multiple times, graphing the results, and engaging in visual analysis, the team predicts that, if they keep providing attention contingent on self injury, the target behavior will continue as before. 

Why it matters: Behavior analysts need to predict what the dependent variable would look like if everything else stayed the same in order to design experiments that demonstrate that an independent variable can change the otherwise predicted outcome. 

Verification

Definition: Verification is demonstrating that baseline levels of behavior would have remained without introducing the independent variable (intervention). Verification as a concept can take several forms within a research design, but the foundational idea is the same. 

Example in clinical context: Let’s take the example of Johnny above. The team moved into the intervention phase. Now his team ignores self injury and they have taught Johnny to  use  an “I want attention” button instead, which is always reinforced with attention. Johnny’s levels of self injury are down significantly! To demonstrate that their intervention, rather than something else (such as medication), was responsible for the change in self injury, Johnny’s team could take the button away and start reinforcing self injury again. If Johnny’s behavior looks similar to what it was at the first baseline phase during the assessment, then that is evidence that the intervention was responsible for the change in behavior. 

Why it matters: It’s important to go beyond educated guesses and actually demonstrate in a logical manner that our interventions are responsible for the change in behavior that the client needs. 

Replication

Definition: Replication is strengthening the case that the independent variable is responsible for changes in behavior by demonstrating it multiple times. 

Example in clinical context: Let’s keep talking about Johnny from before. His team could strengthen the probability that their intervention was responsible for the change in the self injury by implementing baseline and intervention/treatment conditions several more times. If the self injury stays low in each intervention phase and high in each baseline phase, each repetition of that change would lend further credibility to the functional relationship. 

Replication can also happen in “smaller” or “bigger” ways. In terms of more micro replications, we can often see within-session replication, such as Johnny engaging in the target behavior every time attention was withdrawn, over and over again, within a single assessment session (e.g., 10 minutes). We also see replication on a broader scale, such as if the researchers utilized similar methodology for many other individuals who also engaged in attention-maintained self injury and found similar treatment results. 

Why it matters: Every time a possible  relationship between two variables is demonstrated, it becomes less and less likely that “chance” or some other factor was primarily responsible for the relationship between the dependent and independent variables. Replication as a concept can take several forms within a research design, but the foundational idea is the same. (See “D-2 distinguish between internal and external validity” for more on how replication ties into validity.)

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Single-Case Intervention Research

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Thanks to remarkable methodological and statistical advances in recent years, single-case design (SCD) research has become a viable and often essential option for researchers in applied psychology, education, and related fields.

This text is a compendium of information and tools for researchers considering SCD research, a methodology in which one or several participants (or other units) comprise a systematically-controlled experimental intervention study. SCD is a highly flexible method of conducting applied intervention research where it is not feasible or practical to collect data from traditional groups of participants.

Initial chapters lay out the key components of SCDs, from articulating dependent variables to documenting methods for achieving experimental control and selecting an appropriate design model. Subsequent chapters show when and how to implement SCDs in a variety of contexts and how to analyze and interpret results.

Authors emphasize key design and analysis tactics, such as randomization, to help enhance the internal validity and scientific credibility of individual studies. This rich resource also includes in-depth descriptions of large-scale SCD research projects being undertaken at key institutions; practical suggestions from journal editors on how to get SCD research published; and detailed instructions for free, user-friendly, web-based randomization software.

Contributors

Series Foreword

Acknowledgements

Introduction: An Overview of Single-Case Intervention Research Thomas R. Kratochwill and Joel R. Levin

I. Methodologies and Analyses

• Constructing Single-Case Research Designs: Logic and Options Robert H. Horner and Samuel L. Odom
• Enhancing the Scientific Credibility of Single-Case Intervention Research: Randomization to the Rescue Thomas R. Kratochwill and Joel R. Levin
• Visual Analysis of Single-Case Intervention Research: Conceptual and Methodological Issues Thomas R. Kratochwill, Joel R. Levin, Robert H. Horner, and Christopher M. Swoboda
• Non-Overlap Analysis for Single-Case Research Richard I. Parker, Kimberly J. Vannest, and John L. Davis
• Single-Case Permutation and Randomization Statistical Tests: Present Status, Promising New Developments John M. Ferron and Joel R. Levin
• The Single-Case Data-Analysis ExPRT ( Excel Package of Randomization Tests ) Joel R. Levin, Anya S. Evmenova, and Boris S. Gafurov
• Using Multilevel Models to Analyze Single-Case Design Data David M. Rindskopf and John M. Ferron
• Analyzing Single-Case Designs: d , G , Hierarchical Models, Bayesian Estimators, Generalized Additive Models, and the Hopes and Fears of Researchers About Analyses William R. Shadish, Larry V. Hedges, James E. Pustejovsky, David M. Rindskopf, Jonathan G. Boyajian, and Kristynn J. Sullivan
• The Role of Single-Case Designs in Supporting Rigorous Intervention Development and Evaluation at the Institute of Education Sciences Jacquelyn A. Buckley, Deborah L. Speece, and Joan E. McLaughlin

II. Reactions From Leaders in the Field

• Single-Case Designs and Large- N Studies: The Best of Both Worlds Susan M. Sheridan
• Using Single-Case Research Designs in Programs of Research Ann P. Kaiser
• Reactions From Journal Editors: Journal of School Psychology Randy G. Floyd
• Reactions From Journal Editors: School Psychology Quarterly Randy W. Kamphaus
• Reactions From Journal Editors: School Psychology Review Matthew K. Burns

About the Editors

Thomas R. Kratochwill, PhD, is Sears Roebuck Foundation–Bascom Professor at the University of Wisconsin–Madison, director of the School Psychology Program, and a licensed psychologist in Wisconsin.

He is the author of more than 200 journal articles and book chapters.  He has written or edited more than 30 books and has made more than 300 professional presentations.

In 1977 he received the Lightner Witmer Award from APA Division 16 (School Psychology). In 1981 he received the Outstanding Research Contributions Award from the Arizona State Psychological Association and in 1995 received an award for Outstanding Contributions to the Advancement of Scientific Knowledge in Psychology from the Wisconsin Psychological Association. Also in 1995, he was the recipient of the Senior Scientist Award from APA Division 16, and the Wisconsin Psychological Association selected his research for its Margaret Bernauer Psychology Research Award.

In 1995, 2001, and 2002 the APA Division 16 journal School Psychology Quarterly selected one of his articles as the best of the year. In 2005 he received the Jack I. Bardon Distinguished Achievement Award from APA Division 16. He was selected as the founding editor of School Psychology Quarterly in 1984 and served as editor of the journal until 1992.

In 2011 Dr. Kratochwill received the Lifetime Achievement Award from the National Register of Health Service Providers in Psychology and the Nadine Murphy Lambert Lifetime Achievement Award from APA Division 16.

Dr. Kratochwill is a fellow of APA Divisions 15 (Educational Psychology), 16, and 53 (Society of Clinical Child and Adolescent Psychology). He is past president of the Society for the Study of School Psychology and was cochair of the Task Force on Evidence-Based Interventions in School Psychology. He was also a member of the APA Task Force on Evidence-Based Practice for Children and Adolescents and the recipient of the 2007 APA Distinguished Career Contributions to Education and Training of Psychologists.

He is the recipient of the University of Wisconsin–Madison Van Hise Outreach Teaching Award and a member of the University's teaching academy. Most recently he has chaired the What Works Clearinghouse Panel for the development of Standards for Single-Case Research Design for review of evidence-based interventions.

Joel R. Levin, PhD, is Professor Emeritus of Educational Psychology, University of Wisconsin–Madison and University of Arizona. He is internationally renowned for his research and writing on educational research methodology and statistical analysis as well as for his career-long program of research on students' learning strategies and study skills, with more than 400 scholarly publications in those domains. Within APA, he is a Fellow of Division 5 (Evaluation, Measurement and Statistics) and Division 15 (Educational Psychology).

From 1986 to 1988 Dr. Levin was head of the Learning and Instruction division of the American Educational Research Association (AERA), from 1991 to 1996 he was editor of APA's Journal of Educational Psychology , and from 2001 to 2003 he was coeditor of the journal Issues in Education: Contributions From Educational Psychology . During 1994–1995 he served as chair of APA's Council of Editors, and from 1993 to 1995 he was an ex-officio representative on APA's Publications and Communications Board.

Dr. Levin chaired an editors' committee that revised the statistical-reporting guidelines sections for the fourth (1994) edition of the APA Publication Manual , and he served on a similar committee that revised the fifth (2001) and sixth (2010) editions of the manual. From 2003 to 2008 he was APA's chief editorial advisor, a position in which he was responsible for mediating editor–author conflicts, managing ethical violations, and making recommendations bearing on all aspects of the scholarly research and publication process.

Dr. Levin has received two article-of-the-year awards from AERA (1972, with Leonard Marascuilo; 1973, with William Rohwer and Anne Cleary) as well as awards from the University of Wisconsin–Madison for both his teaching and his research (1971 and 1980). In 1992 he was presented with a University of Wisconsin–Madison award for his combined research, teaching, and professional service contributions, followed in 1996 by a prestigious University of Wisconsin–Madison named professorship (Julian C. Stanley Chair).

In 1997 the University of Wisconsin–Madison's School of Education honored Dr. Levin with a distinguished career award, and in 2002 he was accorded APA Division 15's highest research recognition, the E. L. Thorndike Award, for his professional achievements. In 2010 AERA's Educational Statisticians Special Interest Group presented him with an award for exceptional contributions to the field of educational statistics, and most recently, in 2013 the editorial board of the Journal of School Psychology selected his 2012 publication (with John Ferron and Thomas Kratochwill) as the Journal's outstanding article of the year.

A well-written and meaningfully structured compendium that includes the foundational and advanced guidelines for conducting accurate single-case intervention designs. Whether you are an undergraduate or a graduate student, or an applied researcher anywhere along the novice-to-expert column, this book promises to be an invaluable addition to your library. —PsycCRITIQUES

Provides valuable information about single case research design for researchers and graduate students, including methodology, statistical analyses, and the opinions of researchers who have been using it. —Doody's Review Service

This is a welcome addition to the libraries of behavioral researchers interested in knowing more about the lives of children inside and outside of school. Kratochwill and Levin and their contributing authors blend the sometimes esoteric issues of the philosophy of science, experimental design, and statistics with the real-life issues of how to get grant funding and publish research. This volume is useful for new and experienced researchers alike. —Ilene S. Schwartz, PhD, professor, University of Washington, Seattle, and director, Haring Center for Research on Inclusive Education, Seattle, WA

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• CREd Library , Research Design and Method

Issues In Single-Subject Research

Kevin p kearns.

• March, 2011

DOI: 10.1044/cred-ssd-ps-cpri005

The following slides accompanied a presentation delivered at ASHA’s Clinical Practice Research Institute.

Data speak, not men…

“Designs have inherent rigor but not all studies using a design are rigorous” — Randy; yesterday

“Illusion of strong evidence…”– Gilbert, McPeek & Mosteller, 1977

Effects of Interpretation Bias on Research Evidence (Kaptchuk, 2003)

• “Good science inevitably embodies a tension between the empiricism of concrete data and the rationalism of deeply held convictions.”
• “…a view that science is totally objective is mythical and ignores the human element.”

Single-Subject Designs: Introduction

• Single subject experimental designs are among the most prevalent used in SLP treatment research. — (Kearns & Thompson, 1991; Thompson, 2006; Schlosser et al, 2004)
• Well designed single subject design studies are now commonly published in our journals as well as in interdisciplinary specialty journals — (Psychology, Neuropsychology, Education , PT, OT…)
• Agencies, including NIH, NIDDR etc., commonly fund conceptually salient and well designed single subject design treatment programs — (Aphasia, AAC, autism…)
• Meta-analyses have been employed to examine the overall impact of single subject studies on the efficacy and efficiency of interventions — (Robey et al., 1999)

• Quality indicators for single-subject designs appear to be less well understood than for group designs (Kratochwill & Stoiber, 2002; APA Div. 12; Horner, Carr, Halle, et al, 2005).
• Common threats to internal and external validity persist in our despite readily available solutions. (Schlosser, 2004; Thomson, 2006)

• Brief introduction to single subject designs
• Identify elements of single designs that contribute to problems with internal validity/experimental control from a reviewer’s perspective
• Discuss solutions for some of these issues; ultimately necessary for publication and external funding

Common Single-Subject Design Strategies

• Single-subject designs are experimental, not observational.
• Subjects “serve as their own controls”; receive both treatment and no-treatment conditions
• Juxtaposition of Baseline (A) phases with Treatment (B) phases provides mechanism for experimental control (internal validity)
• Control is based on within and across subject replication

Multiple- Baseline: Across Behaviors

Treatment vs No-treatment comparisons

• Examine efficacy of treatment relative to no treatment
• Multiple baselines/ variants; Withdrawal/ reversals

Component Assessment

• Relative contribution of treatment components
• Interaction Designs (variant of reversals)

Successive Level Analysis

• Examine successive levels of treatment
• Multiple Probe; Changing Criterion

Treatment – Treatment Comparisons

• Alternating Treatments (mixed m b )

ABAB Withdrawal Design

ATD-MB comparison: Broca’s aphasia

Internal Validity

• Operational specificity; reliability of IV, DV; treatment integrity; appropriate design
• Artifact, Bias
• Visual analysis of ‘control’: Loss of baseline (unstable; drifting trend); W/I and across phase changes: Level, Slope, Trend
• Replicated treatment effects: three demonstrations of the effect at three points in time

Visual-Graphic Analysis

• Level (on the ordinate; %..)
• Slope (stable, increasing, decreasing)
• Trend over time (variable; changes with phases; overlapping.)
• Overlap, immediacy of effect, similarity of effect for similar phases
• Correlation of change and phase change

Research on Visual Inspection of Single-Subject Data (Franklin et al, 1996; Robey et al, 1999)

• Low level of inter-rater agreement: De Prospero & Cohen (1979) Reported R = .61 among behavioral journal reviewers
• Reliability and validity of visual inspection can be improved with training (Hagopian et al, 1997)
• Visual aids (trend lines) may have produced only modest increase in reliability
• Traditional statistical analyses (eg. Binomial test) are highly affected by serial dependence (Crosbie, 1993)

Serial Dependence/Autocorrelation

• The level of behavior at one point in time is influenced by or correlated with the level of behavior at another point in time
• Autocorrelation biases interpretation and leads to Type I errors (falsely concluding a treatment effect exists; positive autocorrelation) and Type II errors (falsely concluding no treatment effect; negative autocorrelation)
• Independence assumption

• ITSACORR: A statistical procedure that controls for autocorrelation (Crosbie, 1993)
• Visual Inspection and Structured Criteria (Fisher, Kelley & Lomas, 2003; JABA)
• SMA bootstrapping approach (Borckardt, et al, 2008; AM Psychologist)
• clinicalresearcher.org

Baseline Measures

• Randomize order or stimulus sets/ conditions
• All treatment stimuli need to be assessed in baseline
• Establish equivalence for subsets of stimuli used as representative
• Avoid false baselines
• A priori stability decisions greatly reduce bias
• At least 7 baseline probes may be needed for reliable and valid visual analysis

S1 ITSACORR results were non-significant

S2 ITSACORR results were sig (F < .05)

Too few data points for valid analysis

Intervention

• Explicit steps; directions….a Manual
• Control for order effects
• Assess integrity of intervention (see Schlosser, 2004)
• One variable rule
• Is treatment intensity: sufficient; typical?
• Performance level (e.g. % correct)
• Maximum allowable length of treatment (but not equal phases)

Dependent Measures

• Use multiple measures
• Try not to collect during treatment sessions
• Probe often (weekly or more)
• Pre-train assistants the scoring code and periodically check for ‘drift’
• Are definitions specific, observable and replicable?

Reliability

• Reliability for both intervention and dependent variable
• Obtain for each phase of the study and adequately sample
• Control for sources of bias including drift and expectancy (ABCs — artifact, bias, and complexity)
• Use point to point reliability when possible
• Calculate probability of chance agreement; critical for periods of high or low responding
• Occurrence and non occurrence reliability

A priori Decisions

Failure to establish and make explicit criteria for guiding procedural and methodological decisions prior to change is a serious threat to internal validity that is difficult.

• Participant selection/ exclusion criteria (report attrition)
• Baseline variability, length
• Phase changes
• Clinical significance
• Generalization

Consider Clinically Meaningful Change

Clinical significance can not be assumed from our perspective alone.

Change in level of performance on any outcome measure, even when effects are large and visually obvious or significant, is an insufficient metric of the impact of experimental treatment on our participants/ patients.

Minimal Clinically Important Difference (MCID) : “the smallest difference in a score that is considered worthwhile or important” (Hays & Woolley, 2000)

Responsiveness of Health Measures (Husted et al., 2000) 1. Distribution based approaches examine internal responsiveness, using distribution/ variability of initial (baseline) scores to examine differences (e.g. Effect size).

2. Anchor based approaches examine external responsiveness by comparing change detected by a dependent measure with an external criterion. For example, specify a level of change that meets “minimal clinically important difference” (MCID).

Anchor-based Responsiveness measures (see Beninato, et al Archives of PMR, 2006) use external criterion as “anchor”

• Compare change score on outcome measure to some other estimate of important change
• Patient’s/Family estimates
• Clinician’s estimates
• Necessary to complete the EBP triangle?

Revisiting Clinically Important Change (Social Validation)

When the perceived change is important to the patient, clinician, researcher, payor or society (Beaton et al., 2001)

Requires that we extend our conceptual frame of reference beyond typical outcome measures and distribution based measures of responsiveness

“Time will tell” — (M. Planck, 1950)

“A new scientific truth does not triumph by convincing its opponents and making them see the light, but rather because its opponents eventually die.” — (Kaptchuk, 2003)

Franklin, R. D., Gorman, B. S., Beasley, T. M. & Allison, D. B. (1996). Graphical display and visual analysis.. Design and Snalysis of Single-Case Research , (pp. 119–158). Lawrence Erlbaum Associates.

Kearns, K. P. & Thompson, C. K. (1991). Technical drift and conceptual myopia: The Merlin effect. Clinical Aphasiology , 19, 31–40

Kevin P Kearns SUNY Fredonia

Presented at the Clinical Practice Research Institute (CPRI). Hosted by the American Speech-Language-Hearing Association Research Mentoring Network.

Copyrighted Material. Reproduced by the American Speech-Language-Hearing Association in the Clinical Research Education Library with permission from the author or presenter.

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Single-Subject Research Designs

Rajiv S. Jhangiani; I-Chant A. Chiang; Carrie Cuttler; and Dana C. Leighton

Learning Objectives

• Describe the basic elements of a single-subject research design.
• 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.

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 10.1, 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 10.1 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.)

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) [1] . 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. There may be a period of adjustment to the treatment during which the behavior of interest becomes more variable and begins to increase or decrease. 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 employed an ABAB reversal design. Figure 10.2 approximates the data for Robbie. 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? Why use an ABA design, for example, rather than a simpler AB design? Notice that an AB design is essentially an interrupted time-series design applied to an individual participant. Recall that one problem with that design is that 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 (assuming that the treatment does not create a permanent effect), 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.

There are close relatives of the basic reversal design that allow for the evaluation of more than one treatment. In a  multiple-treatment reversal design , a baseline phase is followed by separate phases in which different treatments are introduced. For example, a researcher might establish a baseline of studying behavior for a disruptive student (A), then introduce a treatment involving positive attention from the teacher (B), and then switch to a treatment involving mild punishment for not studying (C). The participant could then be returned to a baseline phase before reintroducing each treatment—perhaps in the reverse order as a way of controlling for carryover effects. This particular multiple-treatment reversal design could also be referred to as an ABCACB design.

In an  alternating treatments design , two or more treatments are alternated relatively quickly on a regular schedule. For example, positive attention for studying could be used one day and mild punishment for not studying the next, and so on. Or one treatment could be implemented in the morning and another in the afternoon. The alternating treatments design can be a quick and effective way of comparing treatments, but only when the treatments are fast acting.

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 child with an intellectual delay, 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. Perhaps something else happened at about the same time as the treatment—for example, the student’s parents might have started rewarding him for good grades. One solution to these problems is to use a  multiple-baseline design , which is represented in Figure 10.3. There are three different types of multiple-baseline designs which we will now consider.

Multiple-Baseline Design Across Participants

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 unlikely to be a coincidence.

As an example, consider a study by Scott Ross and Robert Horner (Ross & Horner, 2009) [2] . 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. 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 the student’s 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—a very unlikely occurrence—to explain their results.

Multiple-Baseline Design Across Behaviors

In another version of the multiple-baseline design, multiple baselines are established for the same participant but for different dependent variables, and the treatment is introduced at a different time for each dependent variable. Imagine, for example, a study on the effect of setting clear goals on the productivity of an office worker who has two primary tasks: making sales calls and writing reports. Baselines for both tasks could be established. For example, the researcher could measure the number of sales calls made and reports written by the worker each week for several weeks. Then the goal-setting treatment could be introduced for one of these tasks, and at a later time the same treatment could be introduced for the other task. The logic is the same as before. If productivity increases on one task after the treatment is introduced, it is unclear whether the treatment caused the increase. But if productivity increases on both tasks after the treatment is introduced—especially when the treatment is introduced at two different times—then it seems much clearer that the treatment was responsible.

Multiple-Baseline Design Across Settings

In yet a third version of the multiple-baseline design, multiple baselines are established for the same participant but in different settings. For example, a baseline might be established for the amount of time a child spends reading during his free time at school and during his free time at home. Then a treatment such as positive attention might be introduced first at school and later at home. Again, if the dependent variable changes after the treatment is introduced in each setting, then this gives the researcher confidence that the treatment is, in fact, responsible for the change.

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. Group data are described using statistics such as means, standard deviations, correlation coefficients, and so on to detect general patterns. Finally, 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 10.4, 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 10.4, 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.

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) [3] . (Note that averaging  across  participants is less common.) Another approach is to compute the  percentage of non-overlapping data  (PND) for each participant (Scruggs & Mastropieri, 2001) [4] . 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 non-overlapping 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.

Image Description

Figure 10.2 long description:  Line graph showing the results of a study with an ABAB reversal design. The dependent variable was low during first baseline phase; increased during the first treatment; decreased during the second baseline, but was still higher than during the first baseline; and was highest during the second treatment phase.  [Return to Figure 10.2]

Figure 10.3 long description:  Three line graphs showing the results of a generic multiple-baseline study, in which different baselines are established and treatment is introduced to participants at different times.

For Baseline 1, treatment is introduced one-quarter of the way into the study. The dependent variable ranges between 12 and 16 units during the baseline, but drops down to 10 units with treatment and mostly decreases until the end of the study, ranging between 4 and 10 units.

For Baseline 2, treatment is introduced halfway through the study. The dependent variable ranges between 10 and 15 units during the baseline, then has a sharp decrease to 7 units when treatment is introduced. However, the dependent variable increases to 12 units soon after the drop and ranges between 8 and 10 units until the end of the study.

For Baseline 3, treatment is introduced three-quarters of the way into the study. The dependent variable ranges between 12 and 16 units for the most part during the baseline, with one drop down to 10 units. When treatment is introduced, the dependent variable drops down to 10 units and then ranges between 8 and 9 units until the end of the study.  [Return to Figure 10.3]

Figure 10.4 long description:  Two graphs showing the results of a generic single-subject study with an ABA design. In the first graph, under condition A, level is high and the trend is increasing. Under condition B, level is much lower than under condition A and the trend is decreasing. Under condition A again, level is about as high as the first time and the trend is increasing. For each change, latency is short, suggesting that the treatment is the reason for the change.

In the second graph, under condition A, level is relatively low and the trend is increasing. Under condition B, level is a little higher than during condition A and the trend is increasing slightly. Under condition A again, level is a little lower than during condition B and the trend is decreasing slightly. It is difficult to determine the latency of these changes, since each change is rather minute, which suggests that the treatment is ineffective.  [Return to Figure 10.4]

• Sidman, M. (1960). Tactics of scientific research: Evaluating experimental data in psychology . Boston, MA: Authors Cooperative. ↵
• Ross, S. W., & Horner, R. H. (2009). Bully prevention in positive behavior support. Journal of Applied Behavior Analysis, 42 , 747–759. ↵
• Fisch, G. S. (2001). Evaluating data from behavioral analysis: Visual inspection or statistical models. Behavioral Processes, 54 , 137–154. ↵
• Scruggs, T. E., & Mastropieri, M. A. (2001). How to summarize single-participant research: Ideas and applications.  Exceptionality, 9 , 227–244. ↵

When the researcher waits until the participant’s behavior in one condition becomes fairly consistent from observation to observation before changing conditions.

The most basic single-subject research design in which the researcher measures the dependent variable in three phases: Baseline, before a treatment is introduced (A); after the treatment is introduced (B); and then a return to baseline after removing the treatment (A). It is often called an ABA design.

Another term for reversal design.

The beginning phase of an ABA design which acts as a kind of control condition in which the level of responding before any treatment is introduced.

In this design the baseline phase is followed by separate phases in which different treatments are introduced.

In this design two or more treatments are alternated relatively quickly on a regular schedule.

In this design, multiple baselines are either established for one participant or one baseline is established for many participants.

This means plotting individual participants’ data, looking carefully at those plots, and making judgments about whether and to what extent the independent variable had an effect on the dependent variable.

This is the percentage of responses in the treatment condition that are more extreme than the most extreme response in a relevant control condition.

Single-Subject Research Designs Copyright © by Rajiv S. Jhangiani; I-Chant A. Chiang; Carrie Cuttler; and Dana C. Leighton is licensed under a Creative Commons Attribution-NonCommercial-ShareAlike 4.0 International License , except where otherwise noted.

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Single Case Research Design

• First Online: 10 November 2021

Cite this chapter

• Stefan Hunziker 3 &
• Michael Blankenagel 3  

4341 Accesses

6 Citations

This chapter addresses the peculiarities, characteristics, and major fallacies of single case research designs. A single case study research design is a collective term for an in-depth analysis of a small non-random sample. The focus on this design is on in-depth. This characteristic distinguishes the case study research from other research designs that understand the individual case as a rather insignificant and interchangeable aspect of a population or sample. Also, researchers find relevant information on how to write a single case research design paper and learn about typical methodologies used for this research design. The chapter closes with referring to overlapping and adjacent research designs.

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Hunziker, S., Blankenagel, M. (2021). Single Case Research Design. In: Research Design in Business and Management. Springer Gabler, Wiesbaden. https://doi.org/10.1007/978-3-658-34357-6_8

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Chapter 10: Single-Subject Research

Overview of Single-Subject Research

Learning Objectives

• Explain what single-subject research is, including how it differs from other types of psychological research.
• Explain what case studies are, including some of their strengths and weaknesses.
• Explain who uses single-subject research and why.

What Is Single-Subject Research?

Single-subject research  is a type of quantitative research that involves studying in detail the behaviour 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 behaviour primarily in terms of group means, standard deviations, and so on. The majority of this textbook 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. Single-subject research, in contrast, focuses on understanding objective behaviour 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 Note 10.5 “The Case of “Anna O.””) and John Watson and Rosalie Rayner’s description of Little Albert (Watson & Rayner, 1920) [1] , 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, 1961) [2] . (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. (p.9)

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.

Assumptions of Single-Subject Research

Again, single-subject research involves studying a small number of participants and focusing intensively on the behaviour of each one. But why take this approach instead of the group approach? There are several 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 behaviour of individual participants. One reason for this is that group research can hide individual differences and generate results that do not represent the behaviour 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 behaviour of a particular individual that is primarily of interest. A school psychologist, for example, might be interested in changing the behaviour 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.

A second assumption of single-subject research is that it is important to discover causal relationships through the manipulation of an independent variable, the careful measurement of a dependent variable, and the control of extraneous variables. For this reason, single-subject research is often considered a type of experimental research with good internal validity. Recall, for example, that Hall and his colleagues measured their dependent variable (studying) many times—first under a no-treatment control condition, then under a treatment condition (positive teacher attention), and then again under the control condition. Because there was a clear increase in studying when the treatment was introduced, a decrease when it was removed, and an increase when it was reintroduced, there is little doubt that the treatment was the cause of the improvement.

A third 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 behaviours and that can be implemented reliably in the real-world contexts in which they occur. This is sometimes referred to as social validity  (Wolf, 1976) [3] . 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 behaviour 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) [4] . He and other researchers then used it to describe how rewards, punishments, and other external factors affect behaviour over time. This work was carried out primarily using nonhuman subjects—mostly rats and pigeons. This approach, which Skinner called the experimental analysis of behaviour —remains an important subfield of psychology and continues to rely almost exclusively on single-subject research. For excellent examples of this work, look at any issue of the  Journal of the Experimental Analysis of Behaviour . By the 1960s, many researchers were interested in using this approach to conduct applied research primarily with humans—a subfield now called  applied behaviour analysis  (Baer, Wolf, & Risley, 1968) [5] . Applied behaviour analysis plays an especially important role in contemporary research on developmental disabilities, education, organizational behaviour, and health, among many other areas. Excellent examples of this work (including the study by Hall and his colleagues) can be found in the  Journal of Applied Behaviour Analysis .

Although most contemporary single-subject research is conducted from the behavioural perspective, it can in principle be used to address questions framed in terms of any theoretical perspective. For example, a studying technique based on cognitive principles of learning and memory could be evaluated by testing it on individual high school students using the single-subject approach. The single-subject approach can also be used by clinicians who take any theoretical perspective—behavioural, cognitive, psychodynamic, or humanistic—to study processes of therapeutic change with individual clients and to document their clients’ improvement (Kazdin, 1982) [6] .

Key Takeaways

• Single-subject research—which involves testing a small number of participants and focusing intensively on the behaviour 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 has been around since the beginning of the field of psychology. Today it is most strongly associated with the behavioural theoretical perspective, but it can in principle be used to study behaviour from any perspective.
• Practice: Find and read a published article in psychology that reports new single-subject research. ( An archive of articles published in the Journal of Applied Behaviour Analysis can be found at http://www.ncbi.nlm.nih.gov/pmc/journals/309/) Write a short summary of the study.
• Describe one problem related to internal validity.
• Describe one problem related to external validity.
• Generate one hypothesis suggested by the case study that might be interesting to test in a systematic single-subject or group study.

Media Attributions

• Pappenheim 1882 by unknown is in the Public Domain .
• Watson, J. B., & Rayner, R. (1920). Conditioned emotional reactions.  Journal of Experimental Psychology, 3 , 1–14. ↵
• Freud, S. (1961).  Five lectures on psycho-analysis . New York, NY: Norton. ↵
• Wolf, M. (1976). Social validity: The case for subjective measurement or how applied behaviour analysis is finding its heart.  Journal of Applied Behaviour Analysis, 11 , 203–214. ↵
• Skinner, B. F. (1938). T he behaviour of organisms: An experimental analysis . New York, NY: Appleton-Century-Crofts. ↵
• Baer, D. M., Wolf, M. M., & Risley, T. R. (1968). Some current dimensions of applied behaviour analysis.  Journal of Applied Behaviour Analysis, 1 , 91–97. ↵
• Kazdin, A. E. (1982).  Single-case research designs: Methods for clinical and applied settings . New York, NY: Oxford University Press. ↵

A type of quantitative research that involves studying the behaviour of each small number of participants in detail.

The study of large numbers of participants and examining their behaviour primarily in terms of group means, standard deviations, and so on.

A detailed description of an individual, which can include both qualitative and quantitative analyses.

The study of strong and consistent effects that can be implemented reliably in the real-world contexts in which they occur.

Laboratory methods that rely on single-subject research; based upon B. F. Skinner’s philosophy of behaviourism which posits that everything organisms do is behaviour.

Starting in the 1960s, researchers began using single-subject techniques to conduct applied research with human subjects.

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