single case study design research

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• Published: 05 April 2024

Single-case experimental designs: the importance of randomization and replication

• René Tanious   ORCID: orcid.org/0000-0002-5466-1002 1 ,
• Rumen Manolov   ORCID: orcid.org/0000-0002-9387-1926 2 ,
• Patrick Onghena 3 &
• Johan W. S. Vlaeyen   ORCID: orcid.org/0000-0003-0437-6665 1  

Nature Reviews Methods Primers volume  4 , Article number:  27 ( 2024 ) Cite this article

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Single-case experimental designs are rapidly growing in popularity. This popularity needs to be accompanied by transparent and well-justified methodological and statistical decisions. Appropriate experimental design including randomization, proper data handling and adequate reporting are needed to ensure reproducibility and internal validity. The degree of generalizability can be assessed through replication.

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Kazdin, A. E. Single-case experimental designs: characteristics, changes, and challenges. J. Exp. Anal. Behav. 115 , 56–85 (2021).

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Shadish, W. & Sullivan, K. J. Characteristics of single-case designs used to assess intervention effects in 2008. Behav. Res. 43 , 971–980 (2011).

Tanious, R. & Onghena, P. A systematic review of applied single-case research published between 2016 and 2018: study designs, randomization, data aspects, and data analysis. Behav. Res. 53 , 1371–1384 (2021).

Ferron, J., Foster-Johnson, L. & Kromrey, J. D. The functioning of single-case randomization tests with and without random assignment. J. Exp. Educ. 71 , 267–288 (2003).

Michiels, B., Heyvaert, M., Meulders, A. & Onghena, P. Confidence intervals for single-case effect size measures based on randomization test inversion. Behav. Res. 49 , 363–381 (2017).

Aydin, O. Characteristics of missing data in single-case experimental designs: an investigation of published data. Behav. Modif. https://doi.org/10.1177/01454455231212265 (2023).

De, T. K., Michiels, B., Tanious, R. & Onghena, P. Handling missing data in randomization tests for single-case experiments: a simulation study. Behav. Res. 52 , 1355–1370 (2020).

Baek, E., Luo, W. & Lam, K. H. Meta-analysis of single-case experimental design using multilevel modeling. Behav. Modif. 47 , 1546–1573 (2023).

Michiels, B., Tanious, R., De, T. K. & Onghena, P. A randomization test wrapper for synthesizing single-case experiments using multilevel models: a Monte Carlo simulation study. Behav. Res. 52 , 654–666 (2020).

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Acknowledgements

R.T. and J.W.S.V. disclose support for the research of this work from the Dutch Research Council and the Dutch Ministry of Education, Culture and Science (NWO gravitation grant number 024.004.016) within the research project ‘New Science of Mental Disorders’ ( www.nsmd.eu ). R.M. discloses support from the Generalitat de Catalunya’s Agència de Gestió d’Ajusts Universitaris i de Recerca (grant number 2021SGR00366).

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Rumen Manolov

Methodology of Educational Sciences Research Group, Faculty of Psychology and Educational Science, KU Leuven, Leuven, Belgium

Patrick Onghena

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Tanious, R., Manolov, R., Onghena, P. et al. Single-case experimental designs: the importance of randomization and replication. Nat Rev Methods Primers 4 , 27 (2024). https://doi.org/10.1038/s43586-024-00312-8

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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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In This Article Expand or collapse the "in this article" section Single-Case Experimental Designs

Introduction, general overviews and primary textbooks.

• Textbooks in Applied Behavior Analysis
• Types of Single-Case Experimental Designs
• Model Building and Randomization in Single-Case Experimental Designs
• Visual Analysis of Single-Case Experimental Designs
• Effect Size Estimates in Single-Case Experimental Designs
• Reporting Single-Case Design Intervention Research

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Single-Case Experimental Designs by S. Andrew Garbacz , Thomas R. Kratochwill LAST REVIEWED: 29 July 2020 LAST MODIFIED: 29 July 2020 DOI: 10.1093/obo/9780199828340-0265

Single-case experimental designs are a family of experimental designs that are characterized by researcher manipulation of an independent variable and repeated measurement of a dependent variable before (i.e., baseline) and after (i.e., intervention phase) introducing the independent variable. In single-case experimental designs a case is the unit of intervention and analysis (e.g., a child, a school). Because measurement within each case is conducted before and after manipulation of the independent variable, the case typically serves as its own control. Experimental variants of single-case designs provide a basis for determining a causal relation by replication of the intervention through (a) introducing and withdrawing the independent variable, (b) manipulating the independent variable across different phases, and (c) introducing the independent variable in a staggered fashion across different points in time. Due to their economy of resources, single-case designs may be useful during development activities and allow for rapid replication across studies.

Several sources provide overviews of single-case experimental designs. Barlow, et al. 2009 includes an overview for the development of single-case experimental designs, describes key considerations for designing and conducting single-case experimental design research, and reviews procedural elements, assessment strategies, and replication considerations. Kazdin 2011 provides detailed coverage of single-case experimental design variants as well as approaches for evaluating data in single-case experimental designs. Kratochwill and Levin 2014 describes key methodological features that underlie single-case experimental designs, including philosophical and statistical foundations and data evaluation. Ledford and Gast 2018 covers research conceptualization and writing, design variants within single-case experimental design, definitions of variables and associated measurement, and approaches to organize and evaluate data. Riley-Tillman and Burns 2009 provides a practical orientation to single-case experimental designs to facilitate uptake and use in applied settings.

Barlow, D. H., M. K. Nock, and M. Hersen, eds. 2009. Single case experimental designs: Strategies for studying behavior change . 3d ed. New York: Pearson.

A comprehensive reference about the process of designing and conducting single-case experimental design studies. Chapters are integrative but can stand alone.

Kazdin, A. E. 2011. Single-case research designs: Methods for clinical and applied settings . 2d ed. New York: Oxford Univ. Press.

A complete overview and description of single-case experimental design variants as well as information about data evaluation.

Kratochwill, T. R., and J. R. Levin, eds. 2014. Single-case intervention research: Methodological and statistical advances . New York: Routledge.

The authors describe in depth the methodological and analytic considerations necessary for designing and conducting research that uses a single-case experimental design. In addition, the text includes chapters from leaders in psychology and education who provide critical perspectives about the use of single-case experimental designs.

Ledford, J. R., and D. L. Gast, eds. 2018. Single case research methodology: Applications in special education and behavioral sciences . New York: Routledge.

Covers the research process from writing literature reviews, to designing, conducting, and evaluating single-case experimental design studies.

Riley-Tillman, T. C., and M. K. Burns. 2009. Evaluating education interventions: Single-case design for measuring response to intervention . New York: Guilford Press.

Focuses on accelerating uptake and use of single-case experimental designs in applied settings. This book provides a practical, “nuts and bolts” orientation to conducting single-case experimental design research.

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Optimizing behavioral health interventions with single-case designs: from development to dissemination

Jesse dallery.

Department of Psychology, University of Florida, P. O. box 112250, Gainesville, FL 32611 USA

Bethany R Raiff

Department of Psychology, Rowan University, Glassboro, USA

Over the past 70 years, single-case design (SCD) research has evolved to include a broad array of methodological and analytic advances. In this article, we describe some of these advances and discuss how SCDs can be used to optimize behavioral health interventions. Specifically, we discuss how parametric analysis, component analysis, and systematic replications can be used to optimize interventions. We also describe how SCDs can address other features of optimization, which include establishing generality and enabling personalized behavioral medicine. Throughout, we highlight how SCDs can be used during both the development and dissemination stages of behavioral health interventions.

Research methods are tools to discover new phenomena, test theories, and evaluate interventions. Many researchers have argued that our research tools have become limited, particularly in the domain of behavioral health interventions [ 1 – 9 ]. The reasons for their arguments vary, but include an overreliance on randomized controlled trials, the slow pace and high cost of such trials, and the lack of attention to individual differences. In addition, advances in mobile and sensor-based data collection now permit real-time, continuous observation of behavior and symptoms over extended durations [ 3 , 10 , 11 ]. Such fine-grained observation can lead to tailoring of treatment based on changes in behavior, which is challenging to evaluate with traditional methods such as a randomized trial.

In light of the limitations of traditional designs and advances in data collection methods, a growing number of researchers have advocated for alternative research designs [ 2 , 7 , 10 ]. Specifically, one family of research designs, known as single-case designs (SCDs), has been proposed as a useful way to establish the preliminary efficacy of health interventions [ 3 ]. In the present article, we recapitulate and expand on this proposal, and argue that they can be used to optimize health interventions.

We begin with a description of what we consider to be a set of criteria, or ideals, for what research designs should accomplish in attempting to optimize an intervention. Admittedly, these criteria are self-serving in the sense that most of them constitute the strengths of SCDs, but they also apply to other research designs discussed in this volume. Next, we introduce SCDs and how they can be used to optimize treatment using parametric and component analyses. We also describe how SCDs can address other features of optimization, which include establishing generality and enabling personalized behavioral medicine. Throughout, we also highlight how these designs can be used during both the development and dissemination of behavioral health interventions. Finally, we evaluate the extent to which SCDs live up to our ideals.

AN OPTIMIZATION IDEAL

During development and testing of a new intervention, our methods should be efficient, flexible, and rigorous. We would like efficient methods to help us establish preliminary efficacy, or “clinically significant patient improvement over the course of treatment” [ 12 ] (p. 137). We also need flexible methods to test different parameters or components of an intervention. Just as different doses of a drug treatment may need to be titrated to optimize effects, different parameters or components of a behavioral treatment may need to be titrated to optimize effects. It should go without saying that we also want our methods to be rigorous, and therefore eliminate or reduce threats to internal validity.

Also, during development, we would like methods that allow us to assess replications of effects to establish the reliability and generality of an intervention. Replications, if done systematically and thoughtfully, can answer questions about for whom and under what conditions an intervention is effective. Answering these questions speaks to the generality of research findings. As Cohen [ 13 ] noted in a seminal article: “For generalization, psychologists must finally rely, as has been done in all the older sciences, on replication” (p. 997). Relying on replications and establishing the conditions under which an intervention works could also lead to more targeted, efficient dissemination efforts.

During dissemination, when an intervention is implemented in clinical practice, we again would like to know if the intervention is producing a reliable change in behavior for a particular individual. (Here, “we” may refer to practitioners in addition to researchers.) With knowledge derived from development and efficacy testing, we may be able to alter components of an intervention that impact its effectiveness. But, ideally, we would like to not only alter but verify whether these components are working. Also, recognizing that behavior change is idiosyncratic and dynamic, we may need methods that allow ongoing tailoring and testing. This may result in a kind of personalized behavioral medicine in which what gets personalized, and when, is determined through experimental analysis.

In addition, during both development and dissemination, we want methods that afford innovation. We should have methods that allow rapid, rigorous testing of new treatments, and which permit incorporating new technologies to assess and treat behavior as they become available. This might be thought of as systematic play. Whatever we call it, it is a hallmark of the experimental attitude in science.

INTRODUCTION TO SINGLE-CASE DESIGNS

SCDs include an array of methods in which each participant, or case, serves as his or her own control. Although these methods are conceptually rooted in the study of cognition and behavior [ 14 ], they are theory-neutral and can be applied to any health intervention. In a typical study, some behavior or symptom is measured repeatedly during all conditions for all participants. The experimenter systematically introduces and withdraws control and intervention conditions, and assesses effects of the intervention on behavior across replications of these conditions within and across participants. Thus, these studies include repeated, frequent assessment of behavior, experimental manipulation of the independent variable (the intervention or components of the intervention), and replication of effects within and across participants.

The main challenge in conducting a single-case experiment is collecting data of the same behavior or symptom repeatedly over time. In other words, a time series must be possible. If behavior or symptoms cannot be assessed frequently, then SCDs cannot be used (e.g., on a weekly basis, at a minimum, for most health interventions). Fortunately, technology is revolutionizing methods to collect data. For example, ecological momentary assessment (EMA) enables frequent input by an end-user into a handheld computer or mobile phone [ 15 ]. Such input occurs in naturalistic settings, and it usually occurs on a daily basis for several weeks to months. EMA can therefore reveal behavioral variation over time and across contexts, and it can document effects of an intervention on an individual’s behavior [ 15 ]. Sensors to record physical activity, medication adherence, and recent drug use also enable the kind of assessment required for single-case research [ 10 , 16 ]. In addition, advances in information technology and mobile phones can permit frequent assessment of behavior or symptoms [ 17 , 18 ]. Thus, SCDs can capitalize on the ability of technology to easily, unobtrusively, and repeatedly assess health behavior [ 3 , 18 , 19 ].

SCDs suffer from several misconceptions that may limit their use [ 20 – 23 ]. First, a single case does not mean “ n of 1.” The number of participants in a typical study is almost always more than 1, usually around 6 but sometimes as many as 20, 40, or more participants [ 24 , 25 ]. Also, the unit of analysis, or “case,” could be individual participants, clinics, group homes, hospitals, health care agencies, or communities [ 1 ]. Given that the unit of analysis is each case (i.e., participant), a single study could be conceptualized as a series of single-case experiments. Perhaps a better label for these designs would be “intrasubject replication designs” [ 26 ]. Second, SCDs are not limited to interventions that produce large, immediate changes in behavior. They can be used to detect small but meaningful changes in behavior and to assess behavior that may change slowly over time (e.g., learning a new skill) [ 27 ]. Third, SCDs are not quasi-experimental designs [ 20 ]. The conventional notions that detecting causal relations requires random assignment and/or random sampling are false [ 26 ]. Single-case experiments are fully experimental and include controls and replications to permit crisp statements about causal relations between independent and dependent variables.

VARIETIES OF SINGLE-CASE DESIGNS

The most relevant SCDs to behavioral health interventions are presented in Table  1 . The table also presents some procedural information and advantages and disadvantages for each design. (The material below is adapted from [ 3 ]) There are also a number of variants of these designs, enabling flexibility in tailoring the design based on practical or empirical considerations [ 27 , 28 ]. For example, there are several variants to circumvent long periods of assessing behavior during baseline conditions, which may be problematic if the behavior is dangerous, before introducing a potentially effective intervention [ 28 ].

Several single-case designs, including general procedures, advantages, and disadvantages

Procedural controls must be in place to make inferences about causal relations, such as clear, operational definitions of the dependent variables, reliable and valid techniques to assess the behavior, and the experimental design must be sufficient to rule out alternative hypotheses for the behavior change. Table  2 presents a summary of methodological and assessment standards to permit conclusions about treatment effects [ 29 , 30 ]. These standards were derived from Horner et al. [ 29 ] and from the recently released What Works Clearinghouse (WWC) pilot standards for evaluating single-case research to inform policy and practice (hereafter referred to as the SCD standards) [ 31 ].

Quality indicators for single-case research [ 29 ]

All of the designs listed in Table  1 entail a baseline period of observation. During this period, the dependent variable is measured repeatedly under control conditions. For example, Dallery, Glenn, and Raiff [ 24 ] used a reversal design to assess effects of an internet-based incentive program to promote smoking cessation, and the baseline phase included self-monitoring, carbon monoxide assessment of smoking status via a web camera, and monetary incentives for submitting videos. The active ingredient in the intervention, incentives contingent on objectively verified smoking abstinence, was not introduced until the treatment phase.

The duration of the baseline and the pattern of the data should be sufficient to predict future behavior. That is, the level of the dependent variable should be stable enough to predict its direction if the treatment was not introduced. If there is a trend in the direction of the anticipated treatment effect during baseline, or if there is too much variability, the ability to detect a treatment effect will be compromised. Thus, stability, or in some cases a trend in the direction opposite the predicted treatment effect, is desirable during baseline conditions.

In some cases, the source(s) of variability can be identified and potentially mitigated (e.g., variability could be reduced by automating data collection, standardizing the setting and time for data collection). However, there may be instances when there is too much variability during baseline conditions, and thus, detecting a treatment effect will not be feasible. There are no absolute standards to define what “too much” variability means [ 27 ]. Excessive variability is a relative term, which is typically determined by a comparison of performance within and between conditions (e.g., between baseline and intervention conditions) in a single-case experiment. The mere presence of variability does not mean that a single-case approach should be abandoned, however. Indeed, identifying the sources of variability and/or assessing new measurement strategies can be evaluated using SCDs. Under these conditions, the outcome of interest is not an increase or a decrease in some behavior or symptom but a reduction in variability. Once accomplished, the researcher has not only learned something useful but is also better prepared to evaluate the effects of an intervention to increase or decrease some health behavior.

REVERSAL DESIGNS

In a reversal design, a treatment is introduced after the baseline period, and then a baseline period is re-introduced, hence, the “reversal” in this design (also known as an ABA design, where “A” is baseline and “B” is treatment). Using only two conditions, such as a pre-post design, is not considered sufficient to demonstrate experimental control because other sources of influence on behavior cannot be ruled out [ 31 , 32 ]. For example, a smoking cessation intervention could coincide with a price increase in cigarettes. By returning to baseline conditions, we could assess and possibly rule out the influence of the price increase on smoking. Researchers also often use a reversal to the treatment condition. Thus, the experiment ends during a treatment period (an ABAB design). Not only is this desirable from the participant’s perspective but it also provides a replication of the main variable of interest—the treatment [ 33 ].

Figure  1 displays an idealized, ABAB reversal design, and each panel shows data from a different participant. Although all participants were exposed to the same four conditions, the duration of the conditions differed because of trends in the conditions. For example, for participant 1, the beginning of the first baseline condition displays a consistent downward trend (in the same direction as the expected text-message treatment effects). If we were to introduce the smoking cessation-related texts after only five or six baseline sessions, it would be unclear if the decrease in smoking was a function of the independent variable. Therefore, continuing the baseline condition until there is no visible trend helps build our confidence about the causal role of the treatment when it is introduced. The immediate decrease in the level of smoking for participant 1 when the treatment is introduced also implicates the treatment. We can also detect, however, an increasing trend in the early portion of the treatment condition. Thus, we need to continue the treatment condition until there is no undesirable trend before returning to the baseline condition. Similar patterns can be seen for participants 2–4. Based on visual analysis of Fig.  1 , we would conclude that treatment is exerting a reliable effect on smoking. But, the meaningfulness of this effect requires additional considerations (see the section below on “ Visual, Statistical, and Social Validity Analysis ”).

Example of a reversal design showing experimental control and replications within and between subjects. Each panel represents a different participant, each of whom experienced two baseline and two treatment conditions

Studies using reversal designs typically include at least four or more participants. The goal is to generate enough replications, both within participants and across participants, to permit a confident statement about causal relations. For example, several studies on incentive-based treatment to promote drug abstinence have used 20 participants in a reversal design [ 24 , 25 ]. According to the SCD standards, there must be a minimum of three replications to support conclusions about experimental control and thus causation. Also, according to the SCD standards, there must be at least three and preferably five data points per phase to allow the researcher to evaluate stability and experimental effects [ 31 ].

There are two potential limitations of reversal designs in the context of behavioral health interventions. First, the treatment must be withdrawn to demonstrate causal relations. Some have raised an ethical objection about this practice [ 11 ]. However, we think that the benefits of demonstrating that a treatment works outweigh the risks of temporarily withdrawing treatment (in most cases). The treatment can also be re-instituted in a reversal design (i.e., an ABAB design). Second, if the intervention produces relatively permanent changes in behavior, then a reversal to pre-intervention conditions may not be possible. For example, a treatment that develops new skills may imply that these skills cannot be “reversed.” Some interventions do not produce permanent change and must remain in effect for behavior change to be maintained, such as some medications and incentive-based procedures. Under conditions where behavior may not return to baseline levels when treatment is withdrawn, alternative designs, such as multiple-baseline designs, should be used.

MULTIPLE-BASELINE DESIGNS

In a multiple-baseline design, the durations of the baselines vary systematically for each participant in a so-called staggered fashion. For example, one participant may start treatment after five baseline days, another after seven baseline days, then nine, and so on. After baseline, treatment is introduced, and it remains until the end of the experiment (i.e., there are no reversals). Like all SCDs, this design can be applied to individual participants, clusters of individuals, health care agencies, and communities. These designs are also referred to as interrupted time-series designs [ 1 ] and stepped wedge designs [ 7 ].

The utility of these designs is derived from demonstrating that change occurs when, and only when, the intervention is directed at a particular participant (or whatever the unit of analysis happens to be [ 28 ]). The influence of other factors, such as idiosyncratic experiences of the individual or self-monitoring (e.g., reactivity), can be ruled out by replicating the effect across multiple individuals. A key to ruling out extraneous factors is a stable enough baseline phase (either no trends or a trend in the opposite direction to the treatment effect). As replications are observed across individuals, and behavior changes when and only when treatment is introduced, confidence that behavior change was caused by the treatment increases.

As noted above, multiple-baseline designs are useful for interventions that teach new skills, where behavior would not be expected to “reverse” to baseline levels. Multiple-baseline designs also obviate the ethical concern about withdrawing treatment (as in a reversal design) or using a placebo control comparison group (as in randomized trials), as all participants are exposed to the treatment with multiple-baseline designs.

Figure  2 illustrates a simple, two-condition multiple-baseline design replicated across four participants. As noted above, the experimenter should introduce treatment only when the data appear stable during baseline conditions. The durations of the baseline conditions are staggered for each participant, and the dependent variable increases when, and only when, the independent variable is introduced for all participants. The SCD standards requires at least six phases (i.e., three baseline and three treatment) with at least five data points per phase [ 31 ]. Figure  2 suggests reliable increases in behavior and that the treatment was responsible for these changes.

Example of a multiple-baseline design showing experimental control and replications between subjects. Each row represents a different participant, each of whom experienced a baseline and treatment. The baseline durations differed across participants

CHANGING CRITERION DESIGN

The changing criterion design is also relevant to optimizing interventions [ 34 ]. In a changing criterion design, a baseline is conducted until stability is attained. Then, a treatment goal is introduced, and goals are made progressively more difficult. Behavior should track the introduction of each goal, thus demonstrating control by the level of the independent variable [ 28 ]. For example, Kurti and Dallery [ 35 ] used a changing criterion design to increase activity in six sedentary adults using an internet-based contingency management program to promote walking. Weekly step count goals were gradually increased across 5-day blocks. The step counts for all six participants increased reliably with each increase in the goals, thereby demonstrating experimental control of the intervention. This design has many of the same benefits of the multiple-baseline design, namely that a reversal is not required for ethical or potentially practical reasons (i.e., irreversible treatment effects).

VISUAL, STATISTICAL, AND SOCIAL VALIDITY ANALYSIS

Analyzing the data from SCDs involves three questions: (a) Is there a reliable effect of the intervention? (b) What is the magnitude of the effect? and (c) Are the results clinically meaningful and socially valid [ 31 ]? Social validity refers to the extent to which the goals, procedures, and results of an intervention are socially acceptable to the client, the researcher or health care practitioner, and society [ 36 – 39 ]. The first two questions can be answered by visual and statistical analysis, whereas the third question requires additional considerations.

The SCD standards prioritizes visual analysis of the time-series data to assess the reliability and magnitude of intervention effects [ 29 , 31 , 40 ]. Clinically significant change in patient behavior should be visible. Visual analysis prioritizes clinically significant change in health-related behavior as opposed to statistically significant change in group behavior [ 13 , 41 , 42 ]. Although several researchers have argued that visual analysis may be prone to elevated rates of type 1 error, such errors may be limited to a narrow range of conditions (e.g., when graphs do not contain contextual information about the nature of the plotted behavioral data) [ 27 , 43 ]. Furthermore, in recent years, training in visual analysis has become more formalized and rigorous [ 44 ]. Perhaps as a result, Kahng and colleagues found high reliability among visual analysts in judging treatment effects based on analysis of 36 ABAB graphs [ 45 ]. The SCD standards recommends four steps and the evaluation of six features of the graphical displays for all participants in a study, which are displayed in Table  3 [ 31 ]. As the visual analyst progresses through the steps, he or she also uses the six features to evaluate effects within and across experimental phases.

Four steps and six outcome measures to evaluate when conducting visual analysis of time-series data

In addition to visual analysis, several regression-based approaches are available to analyze time-series data, such as autoregressive models, robust regression, and hierarchical linear modeling (HLM) [ 46 – 49 ]. A variety of non-parametric statistics are also available [ 27 ]. Perhaps because of the proliferation of statistical methods, there is a lack of consensus about which methods are most appropriate in light of different properties of the data (e.g., the presence of trends and autocorrelation [ 43 , 50 ], the number of data points collected, etc.). A discussion of statistical techniques is beyond the scope of this paper. We recommend Kazdin’s [ 27 ] or Barlow and colleague’s [ 28 ] textbooks as useful resources regarding statistical analysis of time-series data. The SCD standards also includes a useful discussion of statistical approaches for data analysis [ 31 ].

A variety of effect size calculations have been proposed for SCDs [ 13 , 51 – 54 ]. Although effect size estimates may allow for rank ordering of most to least effective treatments [ 55 ], most estimates do not provide metrics that are comparable to effect sizes derived from group designs [ 31 ]. However, one estimate that provides metrics comparable to group designs has been developed and tested by Shadish and colleagues [ 56 , 57 ]. They describe a standardized mean difference statistic ( d ) that is equivalent to the more conventional d in between-groups experiments. The d statistic can also be used to compute power based on the number of observations in each condition and the number of cases in an experiment [ 57 ]. In addition, advances in effect size estimates has led to several meta-analyses of results from SCDs [ 48 , 58 – 61 ]. Zucker and associates [ 62 ] explored Bayesian mixed-model strategy to combining SCDs using, which allowed population-level claims about the merits of different intervention strategies.

Determining whether the results are clinically meaningful and socially valid can be informed by visual and most forms of statistical analysis (i.e., not null-hypothesis significance testing) [ 42 , 63 ]. One element in judging social validity concerns the clinical meaningfulness of the magnitude of behavior change. This judgment can be made by the researcher or clinician in light of knowledge of the subject matter, and perhaps by the client being treated. Depending on factors such as the type of behavior and the way in which change is measured, the judgment can also be informed by previous research on a minimal clinically important difference (MCID) for the behavior or symptom under study [ 64 , 65 ]. The procedures used to generate the effect also require consideration. Intrusive procedures may be efficacious yet not acceptable. The social validity of results and procedures should be explicitly assessed when conducting SCD research, and a variety of tools have emerged to facilitate such efforts [ 37 ]. Social validity assessment should also be viewed as a process [ 37 ]. That is, it can and should be assessed at various time points as an intervention is developed, refined, and eventually implemented. Social validity may change as the procedures and results of an intervention are improved and better appreciated in the society at large.

OPTIMIZATION METHODS AND SINGLE-CASE DESIGNS

The SCDs described above provide an efficient way to evaluate the effects of a behavioral intervention. However, in most of the examples above, the interventions were held constant during treatment periods; that is, they were procedurally static (cf. [ 35 ]). This is similar to a randomized trial, in which all components of an intervention are delivered all at once and held constant throughout the study. However, the major difference between the examples above and traditional randomized trials is efficiency: SCDs usually require less time and fewer resources to demonstrate that an intervention can change behavior. Nevertheless, a single, procedurally static single-case experiment does not optimize treatment beyond showing whether or not it works.

One way to make initial efficacy testing more dynamic would be to conduct a series of single-case experiments in which aspects of the treatment are systematically explored. For example, a researcher could assess effects of different frequencies, timings, or tailoring dimensions of a text-based intervention to promote physical activity. Such manipulation could also be conducted in separate experiments conducted by the same or different researchers. Some experiments may reveal larger effects than others, which could then lead to further replications of the effects of the more promising intervention elements. This iterative development process, with a focus on systematic manipulation of treatment elements and replications of effects within and across experiments, could lead to an improved intervention within a few years’ time. Arguably, this process could yield more clinically useful information than a procedurally static randomized trial conducted over the same period [ 5 , 17 ].

To further increase the efficiency of optimizing treatment, different components or parameters of an intervention can be systematically evaluated within and across single-case experiments. There are two ways to optimize treatment using these methods: parametric and component analyses.

PARAMETRIC ANALYSIS

Parametric analysis involves exposing participants to a range of values of the independent variable, as opposed to just one or two values. To qualify as a parametric analysis, three is the minimum number of values that must be evaluated, as this number is the minimum to evaluate the function form relating the independent to the dependent variable. One goal of a parametric analysis is to identify the optimal value that produces a behavioral outcome. Another goal is to identify general patterns of behavior engendered by a range of values of the independent variable [ 26 , 63 ].

Many behavioral health interventions can be delivered at different levels [ 66 ] and are therefore amenable to parametric analysis. For example, text-based prompts can be delivered at different frequencies, incentives can be delivered at different magnitudes and frequencies, physical activity can occur at different frequencies and intensities, engagement in a web-based program can occur at different levels, medications can be administered at different doses and frequencies, and all of the interventions could be delivered for different durations.

The repeated measures, and resulting time-series data, that are inherent to all SCDs (e.g., reversal and multiple-baseline designs) make them useful designs to conduct parametric analyses. For example, two doses of a medication, low versus high, labeled B and C, respectively, could be assessed using a reversal design [ 67 ]. There may be several possible sequences to conduct the assessment such as ABCBCA or ABCABCA. If C is found to be more effective of the two, it might behoove the researcher to replicate this condition using an ABCBCAC design. A multiple baseline across participants could also be conducted to assess the two doses, one dose for each participant, but this approach may be complicated by individual variability in medication effects. Instead, the multiple-baseline approach could be used on a within-subject basis, where the durations of not just the baselines but of the different dose conditions are varied across participants [ 68 ].

Guyatt and colleagues [ 5 ] provide an excellent discussion about how parametric analysis can be used to optimize an intervention. The intervention was amitriptyline for the treatment of fibrositis. The logic and implications of the research tactics, however, also apply to other interventions that have parametric dimensions. At the time that the research was conducted, a dose of 50 mg/day was the standard recommendation for patients. To determine whether this dose was optimal for a given individual, the researchers first exposed participants to low doses, and if no response was noted relative to placebo, then they systematically increased the dose until a response was observed, or until they reached the maximum of 50 mg/day. In general, their method involved a reversal design in which successively higher doses alternated with placebo. So, for example, if one participant did not respond to a low dose, then doses might be increased to generate an ABCD design, where each successive letter represents a higher dose (other sequences were arranged as well). Parametrically examining doses in this way, and examining individual subject data, the researchers found that some participants responded favorably at lower doses than 50 mg/day (e.g., 10 or 20 mg/day). This was an important finding because the higher doses often produced unwanted side effects. Once optimal doses were identified for individuals, the researchers were able to conduct further analyses using a reversal design, exposing them to either their optimal dose or placebo on different days.

Guyatt and colleagues also investigated the minimum duration of treatment necessary to detect an effect [ 5 ]. Initially, all participants were exposed to the medication for 4 weeks. Visual analysis of the time-series data revealed that medication effects were apparent within about 1–2 weeks of exposure, making a 4-week trial unnecessary. This discovery was replicated in a number of subjects and led them to optimize future, larger studies by only conducting a 2-week intervention. Investigating different treatment durations, such as this, is also a parametric analysis.

Parametric analysis can detect effects that may be missed using a standard group design with only one or two values of the independent variable. For example, in the studies conducted by Guyatt and colleagues [ 5 ], if only the lowest dose of amitriptyline had been investigated using a group approach, the researchers may have incorrectly concluded that the intervention was ineffective because this dose only worked for some individuals. Likewise, if only the highest dose had been investigated, it may have been shown to be effective, but potentially more individuals would have experienced unnecessary side effects (i.e., the results would have low social validity for these individuals). Perhaps most importantly, in contrast to what is typically measured in a group design (e.g., means, confidence intervals, etc.), optimizing treatment effects is fundamentally a question about an individual ’ s behavior.

COMPONENT ANALYSIS

A component analysis is “any experiment designed to identify the active elements of a treatment condition, the relative contributions of different variables in a treatment package, and/or the necessary and sufficient components of an intervention” [ 69 ]. Behavioral health interventions often entail more than one potentially active treatment element. Determining the active elements may be important to increase dissemination potential and decrease cost. Single-case research designs, in particular the reversal and multiple-baseline designs, may be used to perform a component analysis. The essential experimental ingredients, regardless of the method, are that the independent variable(s) are systematically introduced and/or withdrawn, combined with replication of effects within and/or between subjects.

There are two main variants of component analyses: the dropout and add-in analyses. In a dropout analysis, the full treatment package is presented following a baseline phase and then components are systematically withdrawn from the package. A limitation of dropout analyses is when components produce irreversible behavior change (i.e., learning a new skill). Given that most interventions seek to produce sustained changes in health-related behavior, dropout analyses may have limited applicability. Instead, in add-in analyses, components can be assessed individually and/or in combination before the full treatment package is assessed [ 69 ]. Thus, a researcher could conduct an ABACAD design, where A is baseline, B and C are the individual components, and D is the combination of the two B and C components. Other sequences are also possible, and which one is selected will require careful consideration. For example, sequence effects should be considered, and researchers could address these effects through counterbalancing, brief “washout” periods, or explicit investigation of these effects [ 26 ]. If sequence effects cannot be avoided, combined SCD and group designs can be used to perform a component analysis. Thus, different components of a treatment package can be delivered between two groups, and within each group, a SCD can be used to assess effects of each combination of components. Although very few component analyses have assessed health behavior or symptoms per se as the outcome measure, there are a variety of behavioral interventions that have been evaluated using component analysis [ 63 ]. For example, Sanders [ 70 ] conducted a component analysis of an intervention to decrease lower back pain (and increase time standing/walking). The analysis consisted of four components: functional analysis of pain behavior (e.g., self-monitoring of pain and the conditions that precede and follow pain), progressive relaxation training, assertion training, and social reinforcement of increased activity. Sanders concluded that both relaxation training and reinforcement of activity were necessary components (see [ 69 ] for a discussion of some limitations of this study).

Several conclusions can be drawn about the effects of the various components in changing behavior. The data should first be evaluated to determine the extent to which the effects of individual components are independent of one another. If they are, then the effects of the components are additive. If they are not, then the effects are multiplicative, or the effects of one component depend on the presence of another component. Figure  3 presents simplified examples of these two possibilities using a reversal design and short data streams (adapted from [ 69 ]). The panel on the left shows additive effects, and the panel on the right shows multiplicative effects. The data also can be analyzed to determine whether each component is necessary and sufficient to produce behavior change. For instance, the panel on the right shows that neither the component labeled X (e.g., self-monitoring of health behavior) nor the component labeled Y (e.g., counseling to change health behavior) is sufficient, and both components are necessary. If two components produce equal changes in behavior, and the same amount of change when both are combined, then either component is sufficient but neither is necessary.

Two examples of possible results from a component analysis. BSL baseline, X first component, Y second component. The panel on the left shows an additive effect of components X and Y, and the panel of the right shows a multiplicative effect of components X and Y

The logic of the component analyses described here is similar to new methods derived from an engineering framework [ 2 , 9 , 71 ]. During the initial stages of intervention development, researchers use factorial designs to allocate participants to different combinations of treatment components. These designs, called fractional factorials because not all combinations of components are tested, can be used to screen promising components of treatment packages. The components tested may be derived from theory or working assumptions about which components and combinations will be of interest, which is the same process used to guide design choices in SCD research. Just as engineering methods seek to isolate and combine active treatment components to optimize interventions, so too do single-case methods. The main difference between approaches is the focus on the individual as the unit of analysis in SCDs.

OPTIMIZING WITH REPLICATIONS AND ESTABLISHING GENERALITY

Another form of optimization is an understanding of the conditions under which an intervention may be successful. These conditions may relate to particular characteristics of the participant (or whatever the unit of analysis happens to be) or to different situations. In other words, optimizing an intervention means establishing its generality.

In the context of single-case research, generality can be demonstrated experimentally in several ways. The most basic way is via direct replication [ 26 ]. Direct replication means conducting the same experiment on the same behavioral problem across several individuals (i.e., a single-case experiment). For example, Raiff and Dallery [ 72 ] achieved a direct replication of the effects of internet-based contingency management (CM) on adherence to glucose testing in four adolescents. One goal of the study was to establish experimental control by the intervention and to minimize as many extraneous factors as possible. Overall, direct replication can help establish generality across participants. It cannot answer questions about generality across settings, behavior change agents, target behaviors, or participants that differ in some way from the original experiment (e.g., to adults diagnosed with type 1 diabetes). Instead, systematic replication can answer these questions. In a systematic replication, the methods from previous direct replication studies are used in a new setting, target behavior, group of participants, and so on [ 73 ]. The Raiff and Dallery study, therefore, was also a systematic replication of effects of internet-based CM to promote smoking cessation to a new problem and to a new group of participants because the procedure had originally been tested with adult smokers [ 24 ]. Effects of internet-based CM for smoking cessation also were systematically replicated in an application to adolescent smokers using a single-case design [ 74 ].

Systematic replication also occurs with parametric manipulation [ 63 ]. In other words, rather than changing the type of participants or setting, we change the value of the independent variable. In addition to demonstrating an optimal effect, parametric analysis may also reveal boundary conditions. These may be conditions under which an intervention no longer has an effect, or points of diminishing returns in which further increases in some parameter produce no further increases in efficacy. For example, if one study was conducted showing that 30 min of moderate exercise produced a decrease in cigarette cravings, a systematic replication, using parametric analysis, might be conducted to determine the effects of other exercise durations (e.g., 5, 30, 60 min) on cigarette craving to identify the boundary parameters (i.e., the minimum and maximum number of minutes of exercise needed to continue to see changes in cigarette craving). Boundary conditions are critical in establishing generality of an intervention. In most cases, the only way to assess boundary conditions is through experimental, parametric analysis of an individual’s behavior.

By carefully choosing the characteristics of the individuals, settings, or other relevant variables in a systematic replication, the researcher can help identify the conditions under which a treatment works. To be sure, as with any new treatment, failures will occur. However, the failure does not detract from the prior successes: “…a procedure can be quite valuable even though it is effective under a narrow range of conditions, as long as we know what those conditions are” [ 75 ]. Such information is important for treatment recommendations in a clinical setting, and scientifically, it means that the conditions themselves may become the subject of experimental analysis.

This discussion leads to a type of generality called scientific generality [ 63 ], which is at the heart of a scientific understanding of behavioral health interventions (or any intervention for that matter). As described by Branch and Pennypacker [ 63 ], scientific generality is characterized by knowledgeable reproducibility, or knowledge of the factors that are required for a phenomenon to occur. Scientific generality can be attained through parametric and component analysis, and through systematic replication. One advantage of a single-case approach to establishing generality is that a series of strategic studies can be conducted with some degree of efficiency. Moreover, the data intimacy afforded by SCDs can help achieve scientific generality about behavioral health interventions.

PERSONALIZED BEHAVIORAL MEDICINE

Personalized behavioral medicine involves three steps: assessing diagnostic, demographic, and other variables that may influence treatment outcomes; assigning an individual to treatment based on this information; and using SCDs to assess and tailor treatment. The first and second steps may be informed by outcomes using SCDs. In addition, the clinician may be in a better position to personalize treatment with knowledge derived from a body of SCD research about generality, boundary conditions, and the factors that are necessary for an effect to occur. (Of course, this information can come from a variety of sources—we are simply highlighting how SCDs may fit in to this process.)

In addition, with advances in genomics and technology-enabled behavioral assessment prior to treatment (i.e., a baseline phase), the clinician may further target treatment to the unique characteristics of the individual [ 76 ]. Genetic testing is becoming more common before prescribing various medications [ 17 ], and it may become useful to predict responses for treatments targeting health behavior. Baseline assessment of behavior using technology such as EMA may allow the clinician to develop a tailored treatment protocol. For example, assessment could reveal the temporal patterning of risky situations, such as drinking alcohol, having an argument, or long periods of inactivity. A text-based support system could be tailored such that the timings of texts are tied to the temporal pattern of the problem behavior. The baseline assessment may also be useful to simply establish whether a problem exists. Also, the data path during baseline may reveal that behavior or symptoms are already improving prior to treatment, which would suggest that other, non-treatment variables are influencing behavior. Perhaps more importantly, compared to self-report, baseline conditions provide a more objective benchmark to assess effects of treatment on behavior and symptoms.

In addition to greater personalization at the start of treatment, ongoing assessment and treatment tailoring can be achieved with SCDs. Hayes [ 77 ] described how parametric and component analyses can be conducted in clinical practice. For example, reversal designs could be used to conduct a component analysis. Two components, or even different treatments, could be systematically introduced alone and together. If the treatments are different, such comparisons would also yield a kind of comparative effectiveness analysis. For example, contingency contracting and pharmacotherapy for smoking cessation could be presented alone using a BCBC design (where B is contracting and C is pharmacotherapy). A combined treatment could also be added, and depending on results, a return to one or the other treatment could follow (e.g., BCDCB, where D is the combined treatment). Furthermore, if a new treatment becomes available, it could be tested relative to an existing standard treatment in the same fashion. One potential limitation of such designs is when a reversal to baseline conditions (i.e., no treatment) is necessary to document treatment effects. Such a return to baseline may be challenging for ethical, reimbursement, and other issues.

Multiple-baseline designs also can be used in clinical contexts. Perhaps the simplest example would be a multiple baseline across individuals with similar problems. Each individual would experience an AB sequence, where the durations of the baseline phases vary. Another possibility is to target different behavior in the same individual in a multiple-baseline across behavior design. For example, a skills training program to improve social behavior could target different aspects of such behavior in a sequential fashion, starting with eye contact, then posture, then speech volume, and so on. If behavior occurs in a variety of distinct settings, the treatment could be sequentially implemented across these settings. Using the same example, treatment could target social behavior at family events, work, and different social settings. It can be problematic if generalization of effects occurs, but it may not necessarily negate the utility of such a design [ 27 ].

Multiple-baseline designs can be used in contexts other than outpatient therapy. Biglan and associates [ 1 ] argued that such designs are particularly useful in community interventions. For example, they described how a multiple baseline across communities and even states could be used to assess effects of changes in drinking age on car crashes. These designs may be especially useful to evaluate technology-based health interventions. A web-based program could be sequentially rolled out to different schools, communities, or other clusters of individuals. Although these research designs are also referred to as interrupted time series and stepped wedge designs, we think it may be more likely for researchers and clinicians to access the rich network of resources, concepts, and analytic tools if these designs are subsumed under the category of multiple-baseline designs.

The systematic comparisons afforded by SCDs can answer several key questions relevant to optimization. The first question a clinician may have is whether a particular intervention will work for his or her client [ 27 ]. It may be that the client has such a unique history and profile of symptoms, the clinician may not be confident about the predictive validity of a particular intervention for his or her client [ 6 ]. SCDs can be used to answer this question. Also, as just described, they can address which of two treatments work better, whether adding two treatments (or components) together works better than either one alone, which level of treatment is optimal (i.e., a parametric analysis), and whether a client prefers one treatment over another (i.e., via social validity assessment). Furthermore, the use of SCDs in practice conforms to the scientist-practitioner ideal espoused by training models in clinical psychology and allied disciplines [ 78 ].

OPTIMIZING FROM DEVELOPMENT TO DISSEMINATION

We are now in a position to evaluate whether SCDs live up to our ideals about optimization. During development, SCDs may obviate some logistical issues in using between-group designs to conduct initial efficacy testing [ 3 , 8 ]. Specifically, the costs and duration needed to conduct a SCD to establish preliminary efficacy would be considerably lower than traditional randomized designs. Riley and colleagues [ 8 ] noted that randomized trials take approximately 5.5 years from the initiation of enrollment to publication, and even longer from the time a grant application is submitted. In addition to establishing whether a treatment works, SCDs have the flexibility to efficiently address which parameters and components are necessary or optimal. In light of traditional methods to establish preliminary efficacy and optimize treatments, Riley and colleagues advocated for “rapid learning research systems.” SCDs are one such system.

Although some logistical issues may be mitigated by using SCDs, they do not necessarily represent easy alternatives to traditional group designs. They require a considerable amount of data per participant (as opposed to a large number of individuals in a group), enough participants to reliably demonstrate experimental effects, and systematic manipulation of variables over a long duration. For the vast majority of research questions, however, SCDs can reduce the resource and time burdens associated with between group designs and allow the investigator to detect important treatment parameters that might otherwise have been missed.

SCDs can minimize or eliminate a number of threats to internal validity. Although a complete discussion of these threats is beyond the scope of this paper (see [ 1 , 27 , 28 ]), the standards listed in Table  1 can provide protection against most threats. For example, the threat known as “testing” refers to the fact that repeated measurement alone may change behavior. To address this, baseline phases need to be sufficiently long, and there must be enough within and/or between participant replications to rule out the effect of testing. Such logic applies to a number of other potential threats (e.g., instrumentation, history, regression to the mean, etc.). In addition, a plethora of new analytic techniques can supplement experimental techniques to make inferences about causal relations. Combining SCD results in meta-analyses can yield information about comparative effects of different treatments, and combing results using Bayesian methods may yield information about likely effects at the population level.

Because of their efficiency and rigor, SCDs permit systematic replications across types of participants, behavior problems, and settings. This research process has also led to “gold-standard,” evidence-based treatments in applied behavior analysis and education [ 29 , 79 ]. More importantly, in several fields, such research has led to scientific understanding of the conditions under which treatment may be effective or ineffective [ 79 , 80 ]. The field of applied behavior analysis, for example, has matured to the extent that individualized assessment of the causes of problem behavior must occur before treatment recommendations.

Our discussion of personalized behavioral medicine highlighted how SCDs can be used in clinical practice to evaluate and optimize interventions. The advent of technology-based assessment makes SCDs much easier to implement. Technology could propel a “super convergence” of SCDs and clinical practice [ 76 ]. Advances in technology-based assessment can also promote the kind of systematic play central to the experimental attitude. It can also allow testing of new interventions as they become available. Such translational efforts can occur in several ways: from laboratory and other controlled settings to clinical practice, from SCD to SCD within clinical practice, and from randomized efficacy trials to clinical practice.

Over the past 70 years, SCD research has evolved to include a broad array of methodological and analytic advances. It also has generated evidence-based practices in health care and related disciplines such as clinical psychology [ 81 ], substance abuse [ 82 , 83 ], education [ 29 ], medicine [ 4 ], neuropsychology [ 30 ], developmental disabilities [ 27 ], and occupational therapy [ 84 ]. Although different methods are required for different purposes, SCDs are ideally suited to optimize interventions, from development to dissemination.

Acknowledgments

We wish to thank Paul Soto for comments on a previous draft of this manuscript. Preparation of this paper was supported in part by Grants P30DA029926 and R01DA023469 from the National Institute on Drug Abuse.

Conflict of interest

The authors have no conflicts of interest to disclose.

Implications

Practitioners: practitioners can use single-case designs in clinical practice to help ensure that an intervention or component of an intervention is working for an individual client or group of clients.

Policy makers: results from a single-case design research can help inform and evaluate policy regarding behavioral health interventions.

Researchers: researchers can use single-case designs to evaluate and optimize behavioral health interventions.

Contributor Information

Jesse Dallery, Phone: +1-352-3920601, Fax: +1-352-392-7985, Email: ude.lfu@yrellad .

Bethany R Raiff, Email: ude.nawor@ffiar .

The Advantages and Limitations of Single Case Study Analysis

As Andrew Bennett and Colin Elman have recently noted, qualitative research methods presently enjoy “an almost unprecedented popularity and vitality… in the international relations sub-field”, such that they are now “indisputably prominent, if not pre-eminent” (2010: 499). This is, they suggest, due in no small part to the considerable advantages that case study methods in particular have to offer in studying the “complex and relatively unstructured and infrequent phenomena that lie at the heart of the subfield” (Bennett and Elman, 2007: 171). Using selected examples from within the International Relations literature[1], this paper aims to provide a brief overview of the main principles and distinctive advantages and limitations of single case study analysis. Divided into three inter-related sections, the paper therefore begins by first identifying the underlying principles that serve to constitute the case study as a particular research strategy, noting the somewhat contested nature of the approach in ontological, epistemological, and methodological terms. The second part then looks to the principal single case study types and their associated advantages, including those from within the recent ‘third generation’ of qualitative International Relations (IR) research. The final section of the paper then discusses the most commonly articulated limitations of single case studies; while accepting their susceptibility to criticism, it is however suggested that such weaknesses are somewhat exaggerated. The paper concludes that single case study analysis has a great deal to offer as a means of both understanding and explaining contemporary international relations.

The term ‘case study’, John Gerring has suggested, is “a definitional morass… Evidently, researchers have many different things in mind when they talk about case study research” (2006a: 17). It is possible, however, to distil some of the more commonly-agreed principles. One of the most prominent advocates of case study research, Robert Yin (2009: 14) defines it as “an empirical enquiry that investigates a contemporary phenomenon in depth and within its real-life context, especially when the boundaries between phenomenon and context are not clearly evident”. What this definition usefully captures is that case studies are intended – unlike more superficial and generalising methods – to provide a level of detail and understanding, similar to the ethnographer Clifford Geertz’s (1973) notion of ‘thick description’, that allows for the thorough analysis of the complex and particularistic nature of distinct phenomena. Another frequently cited proponent of the approach, Robert Stake, notes that as a form of research the case study “is defined by interest in an individual case, not by the methods of inquiry used”, and that “the object of study is a specific, unique, bounded system” (2008: 443, 445). As such, three key points can be derived from this – respectively concerning issues of ontology, epistemology, and methodology – that are central to the principles of single case study research.

First, the vital notion of ‘boundedness’ when it comes to the particular unit of analysis means that defining principles should incorporate both the synchronic (spatial) and diachronic (temporal) elements of any so-called ‘case’. As Gerring puts it, a case study should be “an intensive study of a single unit… a spatially bounded phenomenon – e.g. a nation-state, revolution, political party, election, or person – observed at a single point in time or over some delimited period of time” (2004: 342). It is important to note, however, that – whereas Gerring refers to a single unit of analysis – it may be that attention also necessarily be given to particular sub-units. This points to the important difference between what Yin refers to as an ‘holistic’ case design, with a single unit of analysis, and an ’embedded’ case design with multiple units of analysis (Yin, 2009: 50-52). The former, for example, would examine only the overall nature of an international organization, whereas the latter would also look to specific departments, programmes, or policies etc.

Secondly, as Tim May notes of the case study approach, “even the most fervent advocates acknowledge that the term has entered into understandings with little specification or discussion of purpose and process” (2011: 220). One of the principal reasons for this, he argues, is the relationship between the use of case studies in social research and the differing epistemological traditions – positivist, interpretivist, and others – within which it has been utilised. Philosophy of science concerns are obviously a complex issue, and beyond the scope of much of this paper. That said, the issue of how it is that we know what we know – of whether or not a single independent reality exists of which we as researchers can seek to provide explanation – does lead us to an important distinction to be made between so-called idiographic and nomothetic case studies (Gerring, 2006b). The former refers to those which purport to explain only a single case, are concerned with particularisation, and hence are typically (although not exclusively) associated with more interpretivist approaches. The latter are those focused studies that reflect upon a larger population and are more concerned with generalisation, as is often so with more positivist approaches[2]. The importance of this distinction, and its relation to the advantages and limitations of single case study analysis, is returned to below.

Thirdly, in methodological terms, given that the case study has often been seen as more of an interpretivist and idiographic tool, it has also been associated with a distinctly qualitative approach (Bryman, 2009: 67-68). However, as Yin notes, case studies can – like all forms of social science research – be exploratory, descriptive, and/or explanatory in nature. It is “a common misconception”, he notes, “that the various research methods should be arrayed hierarchically… many social scientists still deeply believe that case studies are only appropriate for the exploratory phase of an investigation” (Yin, 2009: 6). If case studies can reliably perform any or all three of these roles – and given that their in-depth approach may also require multiple sources of data and the within-case triangulation of methods – then it becomes readily apparent that they should not be limited to only one research paradigm. Exploratory and descriptive studies usually tend toward the qualitative and inductive, whereas explanatory studies are more often quantitative and deductive (David and Sutton, 2011: 165-166). As such, the association of case study analysis with a qualitative approach is a “methodological affinity, not a definitional requirement” (Gerring, 2006a: 36). It is perhaps better to think of case studies as transparadigmatic; it is mistaken to assume single case study analysis to adhere exclusively to a qualitative methodology (or an interpretivist epistemology) even if it – or rather, practitioners of it – may be so inclined. By extension, this also implies that single case study analysis therefore remains an option for a multitude of IR theories and issue areas; it is how this can be put to researchers’ advantage that is the subject of the next section.

Having elucidated the defining principles of the single case study approach, the paper now turns to an overview of its main benefits. As noted above, a lack of consensus still exists within the wider social science literature on the principles and purposes – and by extension the advantages and limitations – of case study research. Given that this paper is directed towards the particular sub-field of International Relations, it suggests Bennett and Elman’s (2010) more discipline-specific understanding of contemporary case study methods as an analytical framework. It begins however, by discussing Harry Eckstein’s seminal (1975) contribution to the potential advantages of the case study approach within the wider social sciences.

Eckstein proposed a taxonomy which usefully identified what he considered to be the five most relevant types of case study. Firstly were so-called configurative-idiographic studies, distinctly interpretivist in orientation and predicated on the assumption that “one cannot attain prediction and control in the natural science sense, but only understanding ( verstehen )… subjective values and modes of cognition are crucial” (1975: 132). Eckstein’s own sceptical view was that any interpreter ‘simply’ considers a body of observations that are not self-explanatory and “without hard rules of interpretation, may discern in them any number of patterns that are more or less equally plausible” (1975: 134). Those of a more post-modernist bent, of course – sharing an “incredulity towards meta-narratives”, in Lyotard’s (1994: xxiv) evocative phrase – would instead suggest that this more free-form approach actually be advantageous in delving into the subtleties and particularities of individual cases.

Eckstein’s four other types of case study, meanwhile, promote a more nomothetic (and positivist) usage. As described, disciplined-configurative studies were essentially about the use of pre-existing general theories, with a case acting “passively, in the main, as a receptacle for putting theories to work” (Eckstein, 1975: 136). As opposed to the opportunity this presented primarily for theory application, Eckstein identified heuristic case studies as explicit theoretical stimulants – thus having instead the intended advantage of theory-building. So-called p lausibility probes entailed preliminary attempts to determine whether initial hypotheses should be considered sound enough to warrant more rigorous and extensive testing. Finally, and perhaps most notably, Eckstein then outlined the idea of crucial case studies , within which he also included the idea of ‘most-likely’ and ‘least-likely’ cases; the essential characteristic of crucial cases being their specific theory-testing function.

Whilst Eckstein’s was an early contribution to refining the case study approach, Yin’s (2009: 47-52) more recent delineation of possible single case designs similarly assigns them roles in the applying, testing, or building of theory, as well as in the study of unique cases[3]. As a subset of the latter, however, Jack Levy (2008) notes that the advantages of idiographic cases are actually twofold. Firstly, as inductive/descriptive cases – akin to Eckstein’s configurative-idiographic cases – whereby they are highly descriptive, lacking in an explicit theoretical framework and therefore taking the form of “total history”. Secondly, they can operate as theory-guided case studies, but ones that seek only to explain or interpret a single historical episode rather than generalise beyond the case. Not only does this therefore incorporate ‘single-outcome’ studies concerned with establishing causal inference (Gerring, 2006b), it also provides room for the more postmodern approaches within IR theory, such as discourse analysis, that may have developed a distinct methodology but do not seek traditional social scientific forms of explanation.

Applying specifically to the state of the field in contemporary IR, Bennett and Elman identify a ‘third generation’ of mainstream qualitative scholars – rooted in a pragmatic scientific realist epistemology and advocating a pluralistic approach to methodology – that have, over the last fifteen years, “revised or added to essentially every aspect of traditional case study research methods” (2010: 502). They identify ‘process tracing’ as having emerged from this as a central method of within-case analysis. As Bennett and Checkel observe, this carries the advantage of offering a methodologically rigorous “analysis of evidence on processes, sequences, and conjunctures of events within a case, for the purposes of either developing or testing hypotheses about causal mechanisms that might causally explain the case” (2012: 10).

Harnessing various methods, process tracing may entail the inductive use of evidence from within a case to develop explanatory hypotheses, and deductive examination of the observable implications of hypothesised causal mechanisms to test their explanatory capability[4]. It involves providing not only a coherent explanation of the key sequential steps in a hypothesised process, but also sensitivity to alternative explanations as well as potential biases in the available evidence (Bennett and Elman 2010: 503-504). John Owen (1994), for example, demonstrates the advantages of process tracing in analysing whether the causal factors underpinning democratic peace theory are – as liberalism suggests – not epiphenomenal, but variously normative, institutional, or some given combination of the two or other unexplained mechanism inherent to liberal states. Within-case process tracing has also been identified as advantageous in addressing the complexity of path-dependent explanations and critical junctures – as for example with the development of political regime types – and their constituent elements of causal possibility, contingency, closure, and constraint (Bennett and Elman, 2006b).

Bennett and Elman (2010: 505-506) also identify the advantages of single case studies that are implicitly comparative: deviant, most-likely, least-likely, and crucial cases. Of these, so-called deviant cases are those whose outcome does not fit with prior theoretical expectations or wider empirical patterns – again, the use of inductive process tracing has the advantage of potentially generating new hypotheses from these, either particular to that individual case or potentially generalisable to a broader population. A classic example here is that of post-independence India as an outlier to the standard modernisation theory of democratisation, which holds that higher levels of socio-economic development are typically required for the transition to, and consolidation of, democratic rule (Lipset, 1959; Diamond, 1992). Absent these factors, MacMillan’s single case study analysis (2008) suggests the particularistic importance of the British colonial heritage, the ideology and leadership of the Indian National Congress, and the size and heterogeneity of the federal state.

Most-likely cases, as per Eckstein above, are those in which a theory is to be considered likely to provide a good explanation if it is to have any application at all, whereas least-likely cases are ‘tough test’ ones in which the posited theory is unlikely to provide good explanation (Bennett and Elman, 2010: 505). Levy (2008) neatly refers to the inferential logic of the least-likely case as the ‘Sinatra inference’ – if a theory can make it here, it can make it anywhere. Conversely, if a theory cannot pass a most-likely case, it is seriously impugned. Single case analysis can therefore be valuable for the testing of theoretical propositions, provided that predictions are relatively precise and measurement error is low (Levy, 2008: 12-13). As Gerring rightly observes of this potential for falsification:

“a positivist orientation toward the work of social science militates toward a greater appreciation of the case study format, not a denigration of that format, as is usually supposed” (Gerring, 2007: 247, emphasis added).

In summary, the various forms of single case study analysis can – through the application of multiple qualitative and/or quantitative research methods – provide a nuanced, empirically-rich, holistic account of specific phenomena. This may be particularly appropriate for those phenomena that are simply less amenable to more superficial measures and tests (or indeed any substantive form of quantification) as well as those for which our reasons for understanding and/or explaining them are irreducibly subjective – as, for example, with many of the normative and ethical issues associated with the practice of international relations. From various epistemological and analytical standpoints, single case study analysis can incorporate both idiographic sui generis cases and, where the potential for generalisation may exist, nomothetic case studies suitable for the testing and building of causal hypotheses. Finally, it should not be ignored that a signal advantage of the case study – with particular relevance to international relations – also exists at a more practical rather than theoretical level. This is, as Eckstein noted, “that it is economical for all resources: money, manpower, time, effort… especially important, of course, if studies are inherently costly, as they are if units are complex collective individuals ” (1975: 149-150, emphasis added).

Limitations

Single case study analysis has, however, been subject to a number of criticisms, the most common of which concern the inter-related issues of methodological rigour, researcher subjectivity, and external validity. With regard to the first point, the prototypical view here is that of Zeev Maoz (2002: 164-165), who suggests that “the use of the case study absolves the author from any kind of methodological considerations. Case studies have become in many cases a synonym for freeform research where anything goes”. The absence of systematic procedures for case study research is something that Yin (2009: 14-15) sees as traditionally the greatest concern due to a relative absence of methodological guidelines. As the previous section suggests, this critique seems somewhat unfair; many contemporary case study practitioners – and representing various strands of IR theory – have increasingly sought to clarify and develop their methodological techniques and epistemological grounding (Bennett and Elman, 2010: 499-500).

A second issue, again also incorporating issues of construct validity, concerns that of the reliability and replicability of various forms of single case study analysis. This is usually tied to a broader critique of qualitative research methods as a whole. However, whereas the latter obviously tend toward an explicitly-acknowledged interpretive basis for meanings, reasons, and understandings:

“quantitative measures appear objective, but only so long as we don’t ask questions about where and how the data were produced… pure objectivity is not a meaningful concept if the goal is to measure intangibles [as] these concepts only exist because we can interpret them” (Berg and Lune, 2010: 340).

The question of researcher subjectivity is a valid one, and it may be intended only as a methodological critique of what are obviously less formalised and researcher-independent methods (Verschuren, 2003). Owen (1994) and Layne’s (1994) contradictory process tracing results of interdemocratic war-avoidance during the Anglo-American crisis of 1861 to 1863 – from liberal and realist standpoints respectively – are a useful example. However, it does also rest on certain assumptions that can raise deeper and potentially irreconcilable ontological and epistemological issues. There are, regardless, plenty such as Bent Flyvbjerg (2006: 237) who suggest that the case study contains no greater bias toward verification than other methods of inquiry, and that “on the contrary, experience indicates that the case study contains a greater bias toward falsification of preconceived notions than toward verification”.

The third and arguably most prominent critique of single case study analysis is the issue of external validity or generalisability. How is it that one case can reliably offer anything beyond the particular? “We always do better (or, in the extreme, no worse) with more observation as the basis of our generalization”, as King et al write; “in all social science research and all prediction, it is important that we be as explicit as possible about the degree of uncertainty that accompanies out prediction” (1994: 212). This is an unavoidably valid criticism. It may be that theories which pass a single crucial case study test, for example, require rare antecedent conditions and therefore actually have little explanatory range. These conditions may emerge more clearly, as Van Evera (1997: 51-54) notes, from large-N studies in which cases that lack them present themselves as outliers exhibiting a theory’s cause but without its predicted outcome. As with the case of Indian democratisation above, it would logically be preferable to conduct large-N analysis beforehand to identify that state’s non-representative nature in relation to the broader population.

There are, however, three important qualifiers to the argument about generalisation that deserve particular mention here. The first is that with regard to an idiographic single-outcome case study, as Eckstein notes, the criticism is “mitigated by the fact that its capability to do so [is] never claimed by its exponents; in fact it is often explicitly repudiated” (1975: 134). Criticism of generalisability is of little relevance when the intention is one of particularisation. A second qualifier relates to the difference between statistical and analytical generalisation; single case studies are clearly less appropriate for the former but arguably retain significant utility for the latter – the difference also between explanatory and exploratory, or theory-testing and theory-building, as discussed above. As Gerring puts it, “theory confirmation/disconfirmation is not the case study’s strong suit” (2004: 350). A third qualification relates to the issue of case selection. As Seawright and Gerring (2008) note, the generalisability of case studies can be increased by the strategic selection of cases. Representative or random samples may not be the most appropriate, given that they may not provide the richest insight (or indeed, that a random and unknown deviant case may appear). Instead, and properly used , atypical or extreme cases “often reveal more information because they activate more actors… and more basic mechanisms in the situation studied” (Flyvbjerg, 2006). Of course, this also points to the very serious limitation, as hinted at with the case of India above, that poor case selection may alternatively lead to overgeneralisation and/or grievous misunderstandings of the relationship between variables or processes (Bennett and Elman, 2006a: 460-463).

As Tim May (2011: 226) notes, “the goal for many proponents of case studies […] is to overcome dichotomies between generalizing and particularizing, quantitative and qualitative, deductive and inductive techniques”. Research aims should drive methodological choices, rather than narrow and dogmatic preconceived approaches. As demonstrated above, there are various advantages to both idiographic and nomothetic single case study analyses – notably the empirically-rich, context-specific, holistic accounts that they have to offer, and their contribution to theory-building and, to a lesser extent, that of theory-testing. Furthermore, while they do possess clear limitations, any research method involves necessary trade-offs; the inherent weaknesses of any one method, however, can potentially be offset by situating them within a broader, pluralistic mixed-method research strategy. Whether or not single case studies are used in this fashion, they clearly have a great deal to offer.

References 

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[1] The paper follows convention by differentiating between ‘International Relations’ as the academic discipline and ‘international relations’ as the subject of study.

[2] There is some similarity here with Stake’s (2008: 445-447) notion of intrinsic cases, those undertaken for a better understanding of the particular case, and instrumental ones that provide insight for the purposes of a wider external interest.

[3] These may be unique in the idiographic sense, or in nomothetic terms as an exception to the generalising suppositions of either probabilistic or deterministic theories (as per deviant cases, below).

[4] Although there are “philosophical hurdles to mount”, according to Bennett and Checkel, there exists no a priori reason as to why process tracing (as typically grounded in scientific realism) is fundamentally incompatible with various strands of positivism or interpretivism (2012: 18-19). By extension, it can therefore be incorporated by a range of contemporary mainstream IR theories.

— Written by: Ben Willis Written at: University of Plymouth Written for: David Brockington Date written: January 2013

Further Reading on E-International Relations

• Identity in International Conflicts: A Case Study of the Cuban Missile Crisis
• Imperialism’s Legacy in the Study of Contemporary Politics: The Case of Hegemonic Stability Theory
• Recreating a Nation’s Identity Through Symbolism: A Chinese Case Study
• Ontological Insecurity: A Case Study on Israeli-Palestinian Conflict in Jerusalem
• Terrorists or Freedom Fighters: A Case Study of ETA
• A Critical Assessment of Eco-Marxism: A Ghanaian Case Study

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Single-Case Design, Analysis, and Quality Assessment for Intervention Research

Affiliation.

• 1 Biomechanics & Movement Science Program, Department of Physical Therapy, University of Delaware, Newark, Delaware (M.A.L., A.B.C., I.B.); and Division of Educational Psychology & Methodology, State University of New York at Albany, Albany, New York (M.M.).
• PMID: 28628553
• PMCID: PMC5492992
• DOI: 10.1097/NPT.0000000000000187

Background and purpose: The purpose of this article is to describe single-case studies and contrast them with case studies and randomized clinical trials. We highlight current research designs, analysis techniques, and quality appraisal tools relevant for single-case rehabilitation research.

Summary of key points: Single-case studies can provide a viable alternative to large group studies such as randomized clinical trials. Single-case studies involve repeated measures and manipulation of an independent variable. They can be designed to have strong internal validity for assessing causal relationships between interventions and outcomes, as well as external validity for generalizability of results, particularly when the study designs incorporate replication, randomization, and multiple participants. Single-case studies should not be confused with case studies/series (ie, case reports), which are reports of clinical management of a patient or a small series of patients.

Recommendations for clinical practice: When rigorously designed, single-case studies can be particularly useful experimental designs in a variety of situations, such as when research resources are limited, studied conditions have low incidences, or when examining effects of novel or expensive interventions. Readers will be directed to examples from the published literature in which these techniques have been discussed, evaluated for quality, and implemented.

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Single-Case Design, Analysis, and Quality Assessment for Intervention Research

Lobo, Michele A. PT, PhD; Moeyaert, Mariola PhD; Baraldi Cunha, Andrea PT, PhD; Babik, Iryna PhD

Biomechanics & Movement Science Program, Department of Physical Therapy, University of Delaware, Newark, Delaware (M.A.L., A.B.C., I.B.); and Division of Educational Psychology & Methodology, State University of New York at Albany, Albany, New York (M.M.).

Correspondence: Michele A. Lobo, PT, PhD, Biomechanics & Movement Science Program, Department of Physical Therapy, University of Delaware, Newark, DE 19713 ( [email protected] ).

This research was supported by the National Institute of Health, Eunice Kennedy Shriver National Institute of Child Health & Human Development (1R21HD076092-01A1, Lobo PI), and the Delaware Economic Development Office (Grant #109).Some of the information in this article was presented at the IV Step Meeting in Columbus, Ohio, June 2016.The authors declare no conflict of interest.

Background and Purpose: 

The purpose of this article is to describe single-case studies and contrast them with case studies and randomized clinical trials. We highlight current research designs, analysis techniques, and quality appraisal tools relevant for single-case rehabilitation research.

Summary of Key Points: 

Single-case studies can provide a viable alternative to large group studies such as randomized clinical trials. Single-case studies involve repeated measures and manipulation of an independent variable. They can be designed to have strong internal validity for assessing causal relationships between interventions and outcomes, as well as external validity for generalizability of results, particularly when the study designs incorporate replication, randomization, and multiple participants. Single-case studies should not be confused with case studies/series (ie, case reports), which are reports of clinical management of a patient or a small series of patients.

Recommendations for Clinical Practice: 

When rigorously designed, single-case studies can be particularly useful experimental designs in a variety of situations, such as when research resources are limited, studied conditions have low incidences, or when examining effects of novel or expensive interventions. Readers will be directed to examples from the published literature in which these techniques have been discussed, evaluated for quality, and implemented.

INTRODUCTION

In this special interest article we present current tools and techniques relevant for single-case rehabilitation research. Single-case (SC) studies have been identified by a variety of names, including “n of 1 studies” and “single-subject” studies. The term “single-case study” is preferred over the previously mentioned terms because previous terms suggest these studies include only 1 participant. In fact, as discussed later, for purposes of replication and improved generalizability, the strongest SC studies commonly include more than 1 participant.

A SC study should not be confused with a “case study/series” (also called “case report”). In a typical case study/series, a single patient or small series of patients is involved, but there is not a purposeful manipulation of an independent variable, nor are there necessarily repeated measures. Most case studies/series are reported in a narrative way, whereas results of SC studies are presented numerically or graphically. 1 , 2 This article defines SC studies, contrasts them with randomized clinical trials, discusses how they can be used to scientifically test hypotheses, and highlights current research designs, analysis techniques, and quality appraisal tools that may be useful for rehabilitation researchers.

In SC studies, measurements of outcome (dependent variables) are recorded repeatedly for individual participants across time and varying levels of an intervention (independent variables). 1–5 These varying levels of intervention are referred to as “phases,” with 1 phase serving as a baseline or comparison, so each participant serves as his/her own control. 2 In contrast to case studies and case series in which participants are observed across time without experimental manipulation of the independent variable, SC studies employ systematic manipulation of the independent variable to allow for hypothesis testing. 1 , 6 As a result, SC studies allow for rigorous experimental evaluation of intervention effects and provide a strong basis for establishing causal inferences. Advances in design and analysis techniques for SC studies observed in recent decades have made SC studies increasingly popular in educational and psychological research. Yet, the authors believe SC studies have been undervalued in rehabilitation research, where randomized clinical trials (RCTs) are typically recommended as the optimal research design to answer questions related to interventions. 7 In reality, there are advantages and disadvantages to both SC studies and RCTs that should be carefully considered to select the best design to answer individual research questions. Although there are a variety of other research designs that could be utilized in rehabilitation research, only SC studies and RCTs are discussed here because SC studies are the focus of this article and RCTs are the most highly recommended design for intervention studies. 7

When designed and conducted properly, RCTs offer strong evidence that changes in outcomes may be related to provision of an intervention. However, RCTs require monetary, time, and personnel resources that many researchers, especially those in clinical settings, may not have available. 8 RCTs also require access to large numbers of consenting participants who meet strict inclusion and exclusion criteria that can limit variability of the sample and generalizability of results. 9 The requirement for large participant numbers may make RCTs difficult to perform in many settings, such as rural and suburban settings, and for many populations, such as those with diagnoses marked by lower prevalence. 8 To rely exclusively on RCTs has the potential to result in bodies of research that are skewed to address the needs of some individuals whereas neglecting the needs of others. RCTs aim to include a large number of participants and to use random group assignment to create study groups that are similar to one another in terms of all potential confounding variables, but it is challenging to identify all confounding variables. Finally, the results of RCTs are typically presented in terms of group means and standard deviations that may not represent true performance of any one participant. 10 This can present as a challenge for clinicians aiming to translate and implement these group findings at the level of the individual.

SC studies can provide a scientifically rigorous alternative to RCTs for experimentally determining the effectiveness of interventions. 1 , 2 SC studies can assess a variety of research questions, settings, cases, independent variables, and outcomes. 11 There are many benefits to SC studies that make them appealing for intervention research. SC studies may require fewer resources than RCTs and can be performed in settings and with populations that do not allow for large numbers of participants. 1 , 2 In SC studies, each participant serves as his/her own comparison, thus controlling for many confounding variables that can impact outcome in rehabilitation research, such as gender, age, socioeconomic level, cognition, home environment, and concurrent interventions. 2 , 11 Results can be analyzed and presented to determine whether interventions resulted in changes at the level of the individual, the level at which rehabilitation professionals intervene. 2 , 12 When properly designed and executed, SC studies can demonstrate strong internal validity to determine the likelihood of a causal relationship between the intervention and outcomes and external validity to generalize the findings to broader settings and populations. 2 , 12 , 13

SINGLE-CASE RESEARCH DESIGNS FOR INTERVENTION RESEARCH

There are a variety of SC designs that can be used to study the effectiveness of interventions. Here we discuss (1) AB designs, (2) reversal designs, (3) multiple baseline designs, and (4) alternating treatment designs, as well as ways replication and randomization techniques can be used to improve internal validity of all of these designs. 1–3 , 12–14

The simplest of these designs is the AB design 15 ( Figure 1 ). This design involves repeated measurement of outcome variables throughout a baseline control/comparison phase (A) and then throughout an intervention phase (B). When possible, it is recommended that a stable level and/or rate of change in performance be observed within the baseline phase before transitioning into the intervention phase. 2 As with all SC designs, it is also recommended that there be a minimum of 5 data points in each phase. 1 , 2 There is no randomization or replication of the baseline or intervention phases in the basic AB design. 2 Therefore, AB designs have problems with internal validity and generalizability of results. 12 They are weak in establishing causality because changes in outcome variables could be related to a variety of other factors, including maturation, experience, learning, and practice effects. 2 , 12 Sample data from a single-case AB study performed to assess the impact of Floor Play intervention on social interaction and communication skills for a child with autism 15 are shown in Figure 1 .

If an intervention does not have carryover effects, it is recommended to use a reversal design . 2 For example, a reversal A 1 BA 2 design 16 ( Figure 2 ) includes alternation of the baseline and intervention phases, whereas a reversal A 1 B 1 A 2 B 2 design 17 ( Figure 3 ) consists of alternation of 2 baseline (A 1 , A 2 ) and 2 intervention (B 1 , B 2 ) phases. Incorporating at least 4 phases in the reversal design (ie, A 1 B 1 A 2 B 2 or A 1 B 1 A 2 B 2 A 3 B 3 ...) allows for a stronger determination of a causal relationship between the intervention and outcome variables because the relationship can be demonstrated across at least 3 different points in time–-change in outcome from A 1 to B 1 , from B 1 to A 2 , and from A 2 to B 2 . 18 Before using this design, however, researchers must determine that it is safe and ethical to withdraw the intervention, especially in cases where the intervention is effective and necessary. 12

A recent study used an ABA reversal SC study to determine the effectiveness of core stability training in 8 participants with multiple sclerosis. 16 During the first 4 weekly data collections, the researchers ensured a stable baseline, which was followed by 8 weekly intervention data points, and concluded with 4 weekly withdrawal data points. Intervention significantly improved participants' walking and reaching performance ( Figure 2 ). 16 This A 1 BA 2 design could have been strengthened by the addition of a second intervention phase for replication (A 1 B 1 A 2 B 2 ). For instance, a single-case A 1 B 1 A 2 B 2 withdrawal design aimed to assess the efficacy of rehabilitation using visuo-spatio-motor cueing for 2 participants with severe unilateral neglect after a severe right hemisphere stroke. 17 Each phase included 8 data points. Statistically significant intervention-related improvement was observed, suggesting that visuo-spatio-motor cueing might be promising for treating individuals with very severe neglect ( Figure 3 ). 17

The reversal design can also incorporate a cross-over design where each participant experiences more than 1 type of intervention. For instance, a B 1 C 1 B 2 C 2 design could be used to study the effects of 2 different interventions (B and C) on outcome measures. Challenges with including more than 1 intervention involve potential carryover effects from earlier interventions and order effects that may impact the measured effectiveness of the interventions. 2 , 12 Including multiple participants and randomizing the order of intervention phase presentations are tools to help control for these types of effects. 19

When an intervention permanently changes an individual's ability, a return-to-baseline performance is not feasible and reversal designs are not appropriate. Multiple baseline designs ( MBDs ) are useful in these situations ( Figure 4 ). 20 Multiple baseline designs feature staggered introduction of the intervention across time: each participant is randomly assigned to 1 of at least 3 experimental conditions characterized by the length of the baseline phase. 21 These studies involve more than 1 participant, thus functioning as SC studies with replication across participants. Staggered introduction of the intervention allows for separation of intervention effects from those of maturation, experience, learning, and practice. For example, a multiple baseline SC study was used to investigate the effect of an antispasticity baclofen medication on stiffness in 5 adult males with spinal cord injury. 20 The subjects were randomly assigned to receive 5 to 9 baseline data points with a placebo treatment before the initiation of the intervention phase with the medication. Both participants and assessors were blind to the experimental condition. The results suggested that baclofen might not be a universal treatment choice for all individuals with spasticity resulting from a traumatic spinal cord injury ( Figure 4 ). 20

The impact of 2 or more interventions can also be assessed via alternating treatment designs ( ATDs ). In ATDs, after establishing the baseline, the experimenter exposes subjects to different intervention conditions administered in close proximity for equal intervals ( Figure 5 ). 22 ATDs are prone to “carryover effects” when the effects of 1 intervention influence the observed outcomes of another intervention. 1 As a result, such designs introduce unique challenges when attempting to determine the effects of any 1 intervention and have been less commonly utilized in rehabilitation. An ATD was used to monitor disruptive behaviors in the school setting throughout a baseline followed by an alternating treatment phase with randomized presentation of a control condition or an exercise condition. 23 Results showed that 30 minutes of moderate to intense physical activity decreased behavioral disruptions through 90 minutes after the intervention. 23 An ATD was also used to compare the effects of commercially available and custom-made video prompts on the performance of multistep cooking tasks in 4 participants with autism. 22 Results showed that participants independently performed more steps with the custom-made video prompts ( Figure 5 ). 22

Regardless of the SC study design, replication and randomization should be incorporated when possible to improve internal and external validity. 11 The reversal design is an example of replication across study phases. The minimum number of phase replications needed to meet quality standards is 3 (A 1 B 1 A 2 B 2 ), but having 4 or more replications is highly recommended (A 1 B 1 A 2 B 2 A 3 ...). 11 , 14 In cases when interventions aim to produce lasting changes in participants' abilities, replication of findings may be demonstrated by replicating intervention effects across multiple participants (as in multiple-participant AB designs), or across multiple settings, tasks, or service providers. When the results of an intervention are replicated across multiple reversals, participants, and/or contexts, there is an increased likelihood that a causal relationship exists between the intervention and the outcome. 2 , 12

Randomization should be incorporated in SC studies to improve internal validity and the ability to assess for causal relationships among interventions and outcomes. 11 In contrast to traditional group designs, SC studies often do not have multiple participants or units that can be randomly assigned to different intervention conditions. Instead, in randomized phase-order designs , the sequence of phases is randomized. Simple or block randomization is possible. For example, with simple randomization for an A 1 B 1 A 2 B 2 design, the A and B conditions are treated as separate units and are randomly assigned to be administered for each of the predefined data collection points. As a result, any combination of A-B sequences is possible without restrictions on the number of times each condition is administered or regard for repetitions of conditions (eg, A 1 B 1 B 2 A 2 B 3 B 4 B 5 A 3 B 6 A 4 A 5 A 6 ). With block randomization for an A 1 B 1 A 2 B 2 design, 2 conditions (eg, A and B) would be blocked into a single unit (AB or BA), randomization of which to different periods would ensure that each condition appears in the resulting sequence more than 2 times (eg, A 1 B 1 B 2 A 2 A 3 B 3 A 4 B 4 ). Note that AB and reversal designs require that the baseline (A) always precedes the first intervention (B), which should be accounted for in the randomization scheme. 2 , 11

In randomized phase start-point designs , the lengths of the A and B phases can be randomized. 2 , 11 , 24–26 For example, for an AB design, researchers could specify the number of time points at which outcome data will be collected (eg, 20), define the minimum number of data points desired in each phase (eg, 4 for A, 3 for B), and then randomize the initiation of the intervention so that it occurs anywhere between the remaining time points (points 5 and 17 in the current example). 27 , 28 For multiple baseline designs, a dual-randomization or “regulated randomization” procedure has been recommended. 29 If multiple baseline randomization depends solely on chance, it could be the case that all units are assigned to begin intervention at points not really separated in time. 30 Such randomly selected initiation of the intervention would result in the drastic reduction of the discriminant and internal validity of the study. 29 To eliminate this issue, investigators should first specify appropriate intervals between the start points for different units, then randomly select from those intervals, and finally randomly assign each unit to a start point. 29

SINGLE-CASE ANALYSIS TECHNIQUES FOR INTERVENTION RESEARCH

The What Works Clearinghouse (WWC) single-case design technical documentation provides an excellent overview of appropriate SC study analysis techniques to evaluate the effectiveness of intervention effects. 1 , 18 First, visual analyses are recommended to determine whether there is a functional relationship between the intervention and the outcome. Second, if evidence for a functional effect is present, the visual analysis is supplemented with quantitative analysis methods evaluating the magnitude of the intervention effect. Third, effect sizes are combined across cases to estimate overall average intervention effects, which contribute to evidence-based practice, theory, and future applications. 2 , 18

Visual Analysis

Traditionally, SC study data are presented graphically. When more than 1 participant engages in a study, a spaghetti plot showing all of their data in the same figure can be helpful for visualization. Visual analysis of graphed data has been the traditional method for evaluating treatment effects in SC research. 1 , 12 , 31 , 32 The visual analysis involves evaluating level, trend, and stability of the data within each phase (ie, within-phase data examination) followed by examination of the immediacy of effect, consistency of data patterns, and overlap of data between baseline and intervention phases (ie, between-phase comparisons). When the changes (and/or variability) in level are in the desired direction, are immediate, readily discernible, and maintained over time, it is concluded that the changes in behavior across phases result from the implemented treatment and are indicative of improvement. 33 Three demonstrations of an intervention effect are necessary for establishing a functional relationship. 1

Within-Phase Examination

Level, trend, and stability of the data within each phase are evaluated. Mean and/or median can be used to report the level, and trend can be evaluated by determining whether the data points are monotonically increasing or decreasing. Within-phase stability can be evaluated by calculating the percentage of data points within 15% of the phase median (or mean). The stability criterion is satisfied if about 85% (80%–90%) of the data in a phase fall within a 15% range of the median (or average) of all data points for that phase. 34

Between-Phase Examination

Immediacy of effect, consistency of data patterns, and overlap of data between baseline and intervention phases are evaluated next. For this, several nonoverlap indices have been proposed that all quantify the proportion of measurements in the intervention phase not overlapping with the baseline measurements. 35 Nonoverlap statistics are typically scaled as percent from 0 to 100, or as a proportion from 0 to 1. Here, we briefly discuss the nonoverlap of all pairs ( NAP ), 36 the extended celeration line ( ECL ), the improvement rate difference ( IRD ), 37 and the TauU , and the TauU-adjusted, TauU adj , 35 as these are the most recent and complete techniques. We also examine the percentage of nonoverlapping data ( PND ) 38 and the two standard deviations band method, as these are frequently used techniques. In addition, we include the percentage of nonoverlapping corrected data ( PNCD )–-an index applying to the PND after controlling for baseline trend. 39

Nonoverlap of All Pairs

Extended Celeration Line

As a consequence, this method depends on a straight line and makes an assumption of linearity in the baseline. 2 , 12

Improvement Rate Difference

This analysis is conceptualized as the difference in improvement rates (IR) between baseline ( IR B ) and intervention phases ( IR T ). 38 The IR for each phase is defined as the number of “improved data points” divided by the total data points in that phase. Improvement rate difference, commonly employed in medical group research under the name of “risk reduction” or “risk difference,” attempts to provide an intuitive interpretation for nonoverlap and to make use of an established, respected effect size, IR B − IR T , or the difference between 2 proportions. 37

TauU and TauU adj

Online calculators might assist researchers in obtaining the TauU and TauU adjusted coefficients ( http://www.singlecaseresearch.org/calculators/tau-u ).

Percentage of Nonoverlapping Data

Two Standard Deviation Band Method

When the stability criterion described earlier is met within phases, it is possible to apply the 2-standard deviation band method. 12 , 41 First, the mean of the data for a specific condition is calculated and represented with a solid line. In the next step, the standard deviation of the same data is computed, and 2 dashed lines are represented: one located 2 standard deviations above the mean and the other 2 standard deviations below. For normally distributed data, few points (<5%) are expected to be outside the 2-standard deviation bands if there is no change in the outcome score because of the intervention. However, this method is not considered a formal statistical procedure, as the data cannot typically be assumed to be normal, continuous, or independent. 41

Statistical Analysis

If the visual analysis indicates a functional relationship (ie, 3 demonstrations of the effectiveness of the intervention effect), it is recommended to proceed with the quantitative analyses, reflecting the magnitude of the intervention effect. First, effect sizes are calculated for each participant (individual-level analysis). Moreover, if the research interest lies in the generalizability of the effect size across participants, effect sizes can be combined across cases to achieve an overall average effect size estimate (across-case effect size).

Note that quantitative analysis methods are still being developed in the domain of SC research 1 and statistical challenges of producing an acceptable measure of treatment effect remain. 14 , 42 , 43 Therefore, the WWC standards strongly recommend conducting sensitivity analysis and reporting multiple effect size estimators. If consistency across different effect size estimators is identified, there is stronger evidence for the effectiveness of the treatment. 1 , 18

Individual-Level Effect Size Analysis

Across-Case Effect Sizes

Two-level modeling to estimate the intervention effects across cases can be used to evaluate across-case effect sizes. 44 , 45 , 50 Multilevel modeling is recommended by the WWC standards because it takes the hierarchical nature of SC studies into account: measurements are nested within cases and cases, in turn, are nested within studies. By conducting a multilevel analysis, important research questions can be addressed (which cannot be answered by single-level analysis of SC study data), such as (1) What is the magnitude of the average treatment effect across cases? (2) What is the magnitude and direction of the case-specific intervention effect? (3) How much does the treatment effect vary within cases and across cases? (4) Does a case and/or study-level predictor influence the treatment's effect? The 2-level model has been validated in previous research using extensive simulation studies. 45 , 46 , 51 The 2-level model appears to have sufficient power (>0.80) to detect large treatment effects in at least 6 participants with 6 measurements. 21

Furthermore, to estimate the across-case effect sizes, the HPS (Hedges, Pustejovsky, and Shadish) , or single-case educational design ( SCEdD)-specific mean difference, index can be calculated. 52 This is a standardized mean difference index specifically designed for SCEdD data, with the aim of making it comparable to Cohen's d of group-comparison designs. The standard deviation takes into account both within-participant and between-participant variability, and is typically used to get an across-case estimator for a standardized change in level. The advantage of using the HPS across-case effect size estimator is that it is directly comparable with Cohen's d for group comparison research, thus enabling the use of Cohen's (1988) benchmarks. 53

Valuable recommendations on SC data analyses have recently been provided. 54 , 55 They suggest that a specific SC study data analytic technique can be chosen on the basis of (1) the study aims and the desired quantification (eg, overall quantification, between-phase quantifications, and randomization), (2) the data characteristics as assessed by visual inspection and the assumptions one is willing to make about the data, and (3) the knowledge and computational resources. 54 , 55 Table 1 lists recommended readings and some commonly used resources related to the design and analysis of single-case studies.

QUALITY APPRAISAL TOOLS FOR SINGLE-CASE DESIGN RESEARCH

Quality appraisal tools are important to guide researchers in designing strong experiments and conducting high-quality systematic reviews of the literature. Unfortunately, quality assessment tools for SC studies are relatively novel, ratings across tools demonstrate variability, and there is currently no “gold standard” tool. 56 Table 2 lists important SC study quality appraisal criteria compiled from the most common scales; when planning studies or reviewing the literature, we recommend readers to consider these criteria. Table 3 lists some commonly used SC quality assessment and reporting tools and references to resources where the tools can be located.

When an established tool is required for systematic review, we recommend use of the WWC tool because it has well-defined criteria and is developed and supported by leading experts in the SC research field in association with the Institute of Education Sciences. 18 The WWC documentation provides clear standards and procedures to evaluate the quality of SC research; it assesses the internal validity of SC studies, classifying them as “meeting standards,” “meeting standards with reservations,” or “not meeting standards.” 1 , 18 Only studies classified in the first 2 categories are recommended for further visual analysis. Also, WWC evaluates the evidence of effect, classifying studies into “strong evidence of a causal relation,” “moderate evidence of a causal relation,” or “no evidence of a causal relation.” Effect size should only be calculated for studies providing strong or moderate evidence of a causal relation.

The Single-Case Reporting Guideline In BEhavioural Interventions (SCRIBE) 2016 is another useful SC research tool developed recently to improve the quality of single-case designs. 57 SCRIBE consists of a 26-item checklist that researchers need to address while reporting the results of SC studies. This practical checklist allows for critical evaluation of SC studies during study planning, manuscript preparation, and review.

Single-case studies can be designed and analyzed in a rigorous manner that allows researchers strength in assessing causal relationships among interventions and outcomes, and in generalizing their results. 2 , 12 These studies can be strengthened via incorporating replication of findings across multiple study phases, participants, settings, or contexts, and by using randomization of conditions or phase lengths. 11 There are a variety of tools that can allow researchers to objectively analyze findings from SC studies. 56 Although a variety of quality assessment tools exist for SC studies, they can be difficult to locate and utilize without experience, and different tools can provide variable results. The WWC quality assessment tool is recommended for those aiming to systematically review SC studies. 1 , 18

SC studies, like all types of study designs, have a variety of limitations. First, it can be challenging to collect at least 5 data points in a given study phase. This may be especially true when traveling for data collection is difficult for participants, or during the baseline phase when delaying intervention may not be safe or ethical. Power in SC studies is related to the number of data points gathered for each participant, so it is important to avoid having a limited number of data points. 12 , 58 Second, SC studies are not always designed in a rigorous manner and, thus, may have poor internal validity. This limitation can be overcome by addressing key characteristics that strengthen SC designs ( Table 2 ). 1 , 14 , 18 Third, SC studies may have poor generalizability. This limitation can be overcome by including a greater number of participants, or units. Fourth, SC studies may require consultation from expert methodologists and statisticians to ensure proper study design and data analysis, especially to manage issues like autocorrelation and variability of data. 2 Fifth, although it is recommended to achieve a stable level and rate of performance throughout the baseline, human performance is quite variable and can make this requirement challenging. Finally, the most important validity threat to SC studies is maturation. This challenge must be considered during the design process to strengthen SC studies. 1 , 2 , 12 , 58

SC studies can be particularly useful for rehabilitation research. They allow researchers to closely track and report change at the level of the individual. They may require fewer resources and, thus, can allow for high-quality experimental research, even in clinical settings. Furthermore, they provide a tool for assessing causal relationships in populations and settings where large numbers of participants are not accessible. For all of these reasons, SC studies can serve as an effective method for assessing the impact of interventions.

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Case study for single institutional review board (sirb) policy.

This fictional case study is based on various real-life scenarios. The exercise includes three sections covering single institutional review board (sIRB) requirements, budgets and protocols, and exception requests—each with associated questions to consider. Review each section, answer the questions, and then check your answer by expanding the question. For background, refer to the NIH Single IRB (sIRB) Policy page where you can find sIRB Frequently Asked Questions , sIRB Determination Workflow , related NIH and Common Rule policy notices, and other resources.

Section 1. sIRB Requirements

In this fictional case study, a principal investigator (PI) submitted a competing R01 application for a due date of September 1, 2017. NIH awarded a grant to the PI's institution. The award supports one ongoing non-exempt human subjects research study that is being conducted at three U.S. sites. Each site relies on its own local IRB for review and approval for the ongoing study. NIH plans to fund the PI's competing renewal award next month. NIH asks the PI for Just-In-Time (JIT) information, including the name of the sIRB of record for the multi-site study.

Sections 1 Questions

1. is the study required to have a sirb why or why not, 2. if the initial irb approval date for the study was december 1, 2019, does this change your answer to question #1, section 2. justifications for an exception to the nih sirb policy.

The PI initially requested a budget for the renewal application without considering the cost associated with an sIRB. The PI now finds that sIRB costs will exceed the proposed budget and sends the Program Official (PO) an exception request to the sIRB requirement. In the request, the PI justifies the exception request by explaining that the original award budget would not cover the cost of an sIRB. Furthermore, because all the participating sites already have their own protocol documents, informed consent documents, and recruitment procedures, the PI believes that the sites are not conducting the same research protocol and therefore are not subject to the NIH sIRB Policy requirement.

Section 2 Questions

3. is lack of money in the award budget sufficient rationale for an sirb exception request, 4. the pi notes that each site has its own protocol which was approved by each site's local irb. the pi contends that each site's unique recruitment procedures and forms mean that each site is conducting a different protocol. are the three sites considered to be conducting different protocols under the nih sirb policy, 5. nih informs the pi that the justification in the exception request is not compelling and will not be considered for an exception. the pi modifies the justification and points out that the new award will be made in one month and it will take at least six to eight months to stand up an sirb for all three sites. the pi expresses concerns that this delay will halt the ongoing research study. is this a sufficient justification for an sirb exception to the nih sirb policy, section 3. next steps.

Ultimately, the PI's exception request is denied for the following reasons:

• NIH does not consider the cost associated with a sIRB as a compelling justification.
• NIH considers the sites to be conducting the same research protocol, even when there are variations in site procedures due to local context considerations. Thus, the NIH sIRB policy requirements apply to all sites in this study.

Section 3 Questions

6. without an exemption, what should the pi do.

The study described in this case is subject to the NIH single IRB Policy requirement.

Increasing Sight-Word Reading Through Peer-Mediated Strategic Incremental Rehearsal

• Research Article
• Published: 23 September 2024

Cite this article

• Destiny N. Coleman 1 ,
• Jessica Blake 1 ,
• Julie C. Martinez 1 ,
• Lizeth Tomas Flores 1 &
• Kathleen B. Aspiranti   ORCID: orcid.org/0000-0003-3523-1338 1  

Strategic incremental rehearsal (SIR), a modified version of the incremental rehearsal strategy, is a flashcard instructional method that is often used to assist struggling readers. Peer-mediated interventions can also increase student abilities and achievement, specifically when used for reading proficiency. However, there is limited empirical research that has examined these two strategies simultaneously. In the current study, we investigated the effectiveness of using a peer tutor when implementing SIR to increase student sight word reading. Researchers conducted the study within a school-based after-school program in a suburban school district. Three 4th- and 5th-grade students who were identified as reading proficiently on grade level served as peer tutors, whereas three 2nd-grade students whose teachers indicated were reading on or below grade level were identified as participants. Peer tutors were taught the SIR strategy and then implemented the intervention using a multiple baseline single case design. Results indicated that using a SIR peer-mediated approach was effective at increasing the number of words read correctly for all participants. Treatment acceptability data suggested that the participants liked the SIR peer-mediated intervention. The application of peer-mediated SIR within the classroom setting is discussed.

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Destiny N. Coleman, Jessica Blake, Julie C. Martinez, Lizeth Tomas Flores & Kathleen B. Aspiranti

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All procedures performed in studies involving human participants were in accordance with the ethical standards of the institutional and/or national research committee and with the 1964 Helsinki declaration and its later amendments or comparable ethical standards. IRB protocol number 81672.

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Destiny N. Coleman, Jessica T. Blake, Julie C. Martinez, Lizeth Tomas Flores, and Kathleen B. Aspiranti declare they have no conflicts of interest.

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Coleman, D.N., Blake, J., Martinez, J.C. et al. Increasing Sight-Word Reading Through Peer-Mediated Strategic Incremental Rehearsal. Behav Analysis Practice (2024). https://doi.org/10.1007/s40617-024-00989-z

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Accepted : 31 July 2024

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DOI : https://doi.org/10.1007/s40617-024-00989-z

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