the family of single case experimental designs

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

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• Model Building and Randomization in Single-Case Experimental Designs
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• 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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• DOI: 10.1162/99608f92.ff9300a8
• Corpus ID: 252168080

The Family of Single-Case Experimental Designs.

• L. Epstein , J. Dallery
• Published in Harvard data science review 8 September 2022

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N-of-1 trials, their reporting guidelines, and the advancement of open science principles, introducing data sciences to n-of-1 designs, statistics, use-cases, the future, and the moniker ‘n-of-1’ trial, personalized (n-of-1) trials for patient-centered treatments of multimorbidity, an r shiny app for a chronic lower back pain study, personalized n-of-1 trial, evaluating technology enhanced learning by using single‐case experimental design: a systematic review, treating taboo thoughts on a psychiatric intensive care unit: a four-phase mixed methods single case experimental design., planning individual and population-based interventions in global health: applying the dea-a framework to promote behavioral, emotional, and/or cognitive change among stakeholders, tiers 1 and 2 of a german mtss: impact of a multiple baseline study on elementary school students with disruptive behavior, a randomized n-of-1 study comparing blood pressure measured on a clothed arm and on an arm with a rolled-up sleeve, assessing the effectiveness of stapp@work, a self-management mobile app, in reducing work stress and preventing burnout: single-case experimental design study, 71 references, single-case design, analysis, and quality assessment for intervention research., enhancing the scientific credibility of single-case intervention research: randomization to the rescue., experimental designs to optimize treatments for individuals: personalized n-of-1 trials., single-case experimental designs to evaluate novel technology-based health interventions, conduct and implementation of personalized trials in research and practice, alternative designs for clinical trials in rare diseases, alternating treatments design: one strategy for comparing the effects of two treatments in a single subject., n of 1 randomized trials for investigating new drugs., single-case experimental designs: characteristics, changes, and challenges., from boulder to stockholm in 70 years: single case experimental designs in clinical research, related papers.

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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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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 Design, Analysis, and Quality Assessment for Intervention Research

Michele a. lobo.

1 Biomechanics & Movement Science Program, Department of Physical Therapy, University of Delaware, Newark, DE, USA

Mariola Moeyaert

2 Division of Educational Psychology & Methodology, State University of New York at Albany, Albany, NY, USA

Andrea Baraldi Cunha

Iryna babik, 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 will 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 and independent variable. They can be designed to have strong internal validity for assessing causal relationships between interventions and outcomes, and 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 one 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, even when researcher 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

The purpose of this article is to 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 one participant. In fact, as will be discussed below, for purposes of replication and improved generalizability, the strongest SC studies commonly include more than one 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 while 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 one 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 in order to select the best design to answer individual research questions. While 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 that 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 while 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 five 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 .

An example of results from a single-case AB study conducted on one participant with autism; two weeks of observation (baseline phase A) were followed by seven weeks of Floor Time Play (intervention phase B). The outcome measure Circles of Communications (reciprocal communication with two participants responding to each other verbally or nonverbally) served as a behavioral indicator of the child’s social interaction and communication skills (higher scores indicating better performance). A statistically significant improvement in Circles of Communication was found during the intervention phase as compared to the baseline. Note that although a stable baseline is recommended for SC studies, it is not always possible to satisfy this requirement, as you will see in Figures 1 – 4 . Data were extracted from Dionne and Martini (2011) 15 utilizing Rohatgi’s WebPlotDigitizer software. 78

If an intervention does not have carry-over 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 two baseline (A 1 , A 2 ) and two intervention (B 1 , B 2 ) phases. Incorporating at least four phases in the reversal design (i.e., 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 three 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

An example of results from a single-case A 1 BA 2 study conducted on eight participants with stable multiple sclerosis (data on three participants were used for this example). Four weeks of observation (baseline phase A 1 ) were followed by eight weeks of core stability training (intervention phase B), then another four weeks of observation (baseline phase A 2 ). Forward functional reach test (the maximal distance the participant can reach forward or lateral beyond arm’s length, maintaining a fixed base of support in the standing position; higher scores indicating better performance) significantly improved during intervention for Participants 1 and 3 without further improvement observed following withdrawal of the intervention (during baseline phase A 2 ). Data were extracted from Freeman et al. (2010) 16 utilizing Rohatgi’s WebPlotDigitizer software. 78

An example of results from a single-case A 1 B 1 A 2 B 2 study conducted on two participants with severe unilateral neglect after a right-hemisphere stroke. Two weeks of conventional treatment (baseline phases A 1, A 2 ) alternated with two weeks of visuo-spatio-motor cueing (intervention phases B 1 , B 2 ). Performance was assessed in two tests of lateral neglect, the Bells Cancellation Test (Figure A; lower scores indicating better performance) and the Line Bisection Test (Figure B; higher scores indicating better performance). There was a statistically significant intervention-related improvement in participants’ performance on the Line Bisection Test, but not on the Bells Test. Data were extracted from Samuel at al. (2000) 17 utilizing Rohatgi’s WebPlotDigitizer software. 78

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 four weekly data collections, the researchers ensured a stable baseline, which was followed by eight weekly intervention data points, and concluded with four 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 two 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 one type of intervention. For instance, a B 1 C 1 B 2 C 2 design could be used to study the effects of two different interventions (B and C) on outcome measures. Challenges with including more than one intervention involve potential carry-over 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 MBDs feature staggered introduction of the intervention across time: each participant is randomly assigned to one of at least 3 experimental conditions characterized by the length of the baseline phase. 21 These studies involve more than one 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 anti-spasticity baclofen medication on stiffness in five adult males with spinal cord injury. 20 The subjects were randomly assigned to receive 5–9 baseline data points with a placebo treatment prior to 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

An example of results from a single-case multiple baseline study conducted on five participants with spasticity due to traumatic spinal cord injury. Total duration of data collection was nine weeks. The first participant was switched from placebo treatment (baseline) to baclofen treatment (intervention) after five data collection sessions, whereas each consecutive participant was switched to baclofen intervention at the subsequent sessions through the ninth session. There was no statistically significant effect of baclofen on viscous stiffness at the ankle joint. Data were extracted from Hinderer at al. (1990) 20 utilizing Rohatgi’s WebPlotDigitizer software. 78

The impact of two 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 “carry-over effects” when the effects of one 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 one 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 multi-step cooking tasks in four participants with autism. 22 Results showed that participants independently performed more steps with the custom-made video prompts ( Figure 5 ). 22

An example of results from a single case alternating treatment study conducted on four participants with autism (data on two participants were used for this example). After the observation phase (baseline), effects of commercially available and custom-made video prompts on the performance of multi-step cooking tasks were identified (treatment phase), after which only the best treatment was used (best treatment phase). Custom-made video prompts were most effective for improving participants’ performance of multi-step cooking tasks. Data were extracted from Mechling at al. (2013) 22 utilizing Rohatgi’s WebPlotDigitizer software. 78

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 three (A 1 B 1 A 2 B 2 ), but having four 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 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 pre-defined 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 (e.g., 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, two conditions (e.g., A and B) would be blocked into a single unit (AB or BA), randomization of which to different time periods would ensure that each condition appears in the resulting sequence more than two times (e.g., 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, (e.g., 20), define the minimum number of data points desired in each phase (e.g., 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 relation 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 contributes to evidence-based practice, theory, and future applications. 2 , 18

Visual Analysis

Traditionally, SC study data are presented graphically. When more than one 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 (i.e., 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 (i.e., 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 relation. 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 (NAP)

Each baseline observation can be paired with each intervention phase observation to make n pairs (i.e., N = n A * n B ). Count the number of overlapping pairs, n o , counting all ties as 0.5. Then define the percent of the pairs that show no overlap. Alternatively, one can count the number of positive (P), negative (N), and tied (T) pairs 2 , 36 :

Extended Celeration Line (ECL)

ECL or split middle line allows control for a positive Phase A trend. Nonoverlap is defined as the proportion of Phase B ( n b ) data that are above the median trend plotted from Phase A data ( n B< sub > Above Median trend A </ sub > ), but then extended into Phase B: ECL = n B Above Median trend A n b ∗ 100

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

Improvement rate difference (IRD)

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. IRD, 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 B , or the difference between two proportions. 37

TauU and TauU adj

Each baseline observation can be paired with each intervention phase observation to make n pairs (i.e., n = n A * n B ). Count the number of positive (P), negative (N), and tied (T) pairs, and use the following formula: TauU = P - N P + N + τ

The TauU adj is an adjustment of TauU for monotonic trend in baseline. Each baseline observation can be paired with each intervention phase observation to make n pairs (i.e., n = n A * n B ). Each baseline observation can be paired with all later baseline observations (n A *(n A -1)/2). 2 , 35 Then the baseline trend can be computed: TauU adf = P - N - S trend P + N + τ ; S trend = P A – NA

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

Percentage of nonoverlapping data (PND)

If anticipating an increase in the outcome, locate the highest data point in the baseline phase and then calculate the percent of the intervention phase data points that exceed it. If anticipating a decrease in the outcome, find the lowest data point in the baseline phase and then calculate the percent of the treatment phase data points that are below it: PND = n B Overlap A n b ∗ 100 . A PND < 50 would mark no observed effect, PND = 50–70 signifies a questionable effect, and PND > 70 suggests the intervention was effective. 40 The percentage of nonoverlapping (PNDC) corrected was proposed in 2009 as an extension of the PND. 39 Prior to applying the PND, a data correction procedure is applied eliminating pre-existing baseline trend. 38

Two Standard Deviation Band Method

When the stability criterion described above is met within phases, it is possible to apply the two 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 two dashed lines are represented: one located two standard deviations above the mean and the other – two standard deviations below. For normally distributed data, few points (less than 5%) are expected to be outside the two standard deviation bands if there is no change in the outcome score due to 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 (i.e., three 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

The most common effect sizes recommended for SC analysis are: 1) standardized mean difference Cohen’s d ; 2) standardized mean difference with correction for small sample sizes Hedges’ g ; and 3) the regression-based approach which has the most potential and is strongly recommended by the WWC standards. 1 , 44 , 45 Cohen’s d can be calculated using following formula: d = X A ¯ - X B ¯ s p , with X A ¯ being the baseline mean, X B ¯ being the treatment mean, and s p indicating the pooled within-case standard deviation. Hedges’ g is an extension of Cohen’s d , recommended in the context of SC studies as it corrects for small sample sizes. The piecewise regression-based approach does not only reflect the immediate intervention effect, but also the intervention effect across time:

i stands for the measurement occasion ( i = 0, 1,… I ). The dependent variable is regressed on a time indicator, T , which is centered around the first observation of the intervention phase, D , a dummy variable for the intervention phase, and an interaction term of these variables. The equation shows that the expected score, Ŷ i , equals β 0 + β 1 T i in the baseline phase, and ( β 0 + β 2 ) + ( β 1 + β 3 ) T i in the intervention phase. β 0 , therefore, indicates the expected baseline level at the start of the intervention phase (when T = 0), whereas β 1 marks the linear time trend in the baseline scores. The coefficient β 2 can then be interpreted as an immediate effect of the intervention on the outcome, whereas β 3 signifies the effect of the intervention across time. The e i ’s are residuals assumed to be normally distributed around a mean of zero with a variance of σ e 2 . The assumption of independence of errors is usually not met in the context of SC studies because repeated measures are obtained within a person. As a consequence, it can be the case that the residuals are autocorrelated, meaning that errors closer in time are more related to each other compared to errors further away in time. 46 – 48 As a consequence, a lag-1 autocorrelation is appropriate (taking into account the correlation between two consecutive errors: e i and e i –1 ; for more details see Verbeke & Molenberghs, (2000). 49 In Equation 1 , ρ indicates the autocorrelation parameter. If ρ is positive, the errors closer in time are more similar; if ρ is negative, the errors closer in time are more different, and if ρ equals zero, there is no correlation between the errors.

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 two-level model has been validated in previous research using extensive simulation studies. 45 , 46 , 51 The two-level model appears to have sufficient power (> .80) to detect large treatment effects in at least six participants with six 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 based on: (1) the study aims and the desired quantification (e.g., overall quantification, between-phase quantifications, randomization, etc.), (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.

Recommend readings and 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 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.

Summary of important single-case study quality appraisal criteria.

Quality assessment and reporting tools related to single-case studies.

When an established tool is required for systematic review, we recommend use of the What Works Clearinghouse (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 two 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 While 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 five 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, while 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 in order 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.

Acknowledgments

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 manuscript was presented at the IV Step Meeting in Columbus, OH, June 2016.

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Single-Case Experimental Design in Rehabilitation: Basic Concepts, Advantages, and Challenges

Affiliation.

• 1 From the Faculty of Rehabilitation Medicine, University of Alberta, Edmonton, Canada (LY, SA-O, DPG); and University of Applied Sciences Osnabrück, Faculty of Economics and Social Sciences, Osnabrück, Germany (SA-O).
• PMID: 36811559
• DOI: 10.1097/PHM.0000000000002215

Single-case experimental design is a family of experimental methods that can be used to examine the efficacy of interventions by testing a small number of patients or cases. This article provides an overview of single-case experimental design research for use in rehabilitation as another option along with traditional group-based research when studying rare cases and rehabilitation interventions of unknown efficacy. Basic concepts related to single-case experimental design and the characteristics of common subtypes ( N-of-1 randomized controlled trial, withdrawal design, multiple-baseline design, multiple-treatment design, changing criterion/intensity design, and alternating treatment design) are introduced. The advantages and disadvantages of each subtype are discussed along with challenges in data analysis and interpretation. Criteria and caveats for interpreting single-case experimental design results and their use in evidence-based practice decisions are discussed. Recommendations are provided for appraising single-case experimental design articles as well as using single-case experimental design principles to improve real-world clinical evaluation.

Copyright © 2023 Wolters Kluwer Health, Inc. All rights reserved.

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Financial disclosure statements have been obtained, and no conflicts of interest have been reported by the authors or by any individuals in control of the content of this article.

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• Published: 18 June 2024

The effect of an online acceptance and commitment intervention on the meaning-making process in cancer patients following hematopoietic cell transplantation: study protocol for a randomized controlled trial enhanced with single-case experimental design

• Aleksandra Kroemeke   ORCID: orcid.org/0000-0001-8707-742X 1 ,
• Joanna Dudek 2 ,
• Marta Kijowska 1 ,
• Ray Owen 3 &
• Małgorzata Sobczyk-Kruszelnicka 4  

Trials volume  25 , Article number:  392 ( 2024 ) Cite this article

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Hematopoietic cell transplantation (HCT) is a highly invasive and life-threatening treatment for hematological neoplasms and some types of cancer that can challenge the patient’s meaning structures. Restoring meaning (i.e., building more flexible and significant explanations of the disease and treatment burden) can be aided by strengthening psychological flexibility by means of an Acceptance and Commitment Therapy (ACT) intervention. Thus, this trial aims to examine the effect of the ACT intervention on the meaning-making process and the underlying mechanisms of change in patients following HCT compared to a minimally enhanced usual care (mEUC) control group. The trial will be enhanced with a single-case experimental design (SCED), where ACT interventions will be compared between individuals with various pre-intervention intervals.

In total, 192 patients who qualify for the first autologous or allogeneic HCT will be recruited for a two-armed parallel randomized controlled trial comparing an online self-help 14-day ACT training to education sessions (recommendations following HCT). In both conditions, participants will receive once a day a short survey and intervention proposal (about 5–10 min a day) in the outpatient period. Double-blinded assessment will be conducted at baseline, during the intervention, immediately, 1 month, and 3 months after the intervention. In addition, 6–9 participants will be invited to SCED and randomly assigned to pre-intervention measurement length (1–3 weeks) before completing ACT intervention, followed by 7-day observations at the 2nd and 3rd post-intervention measure. The primary outcome is meaning-related distress. Secondary outcomes include psychological flexibility, meaning-making coping, meanings made, and well-being as well as global and situational meaning.

This trial represents the first study that integrates the ACT and meaning-making frameworks to reduce meaning-related distress, stimulate the meaning-making process, and enhance the well-being of HCT recipients. Testing of an intervention to address existential concerns unique to patients undergoing HCT will be reinforced by a statistically rigorous idiographic approach to see what works for whom and when. Since access to interventions in the HCT population is limited, the web-based ACT self-help program could potentially fill this gap.

Trial registration

ClinicalTrials.gov ID: NCT06266182. Registered on February 20, 2024.

Peer Review reports

Administrative information

Note: the numbers in curly brackets in this protocol refer to SPIRIT checklist item numbers. The order of the items has been modified to group similar items (see http://www.equator-network.org/reporting-guidelines/spirit-2013-statement-defining-standard-protocol-items-for-clinical-trials/ ).

Introduction

Background and rationale {6a}.

Hematologic neoplasms (e.g., lymphomas or acute leukemias) due to unique and sometimes increased challenges are highly stressful conditions. Treatment-related challenges can impede the realization of life goals and violate general beliefs and a sense of meaning as defined by the integrative meaning-making model [ 1 ]. A significant point on the trajectory of coping, challenging the patient meaning structures, may be hematopoietic cell transplantation (HCT). HCT is a highly invasive and life-threatening treatment for hematological neoplasms and some types of cancer (e.g., testicular cancer). In the acute phase, HCT involves the destruction of the patient hematopoietic system through radio and/or chemotherapy and then its restoration via autologous or allogeneic cell transplantation [ 2 , 3 ]. During in- and outpatient conditions, patients usually experience burdensome adverse effects and have to follow strong medical regimens [ 2 , 4 ]. Evidence suggests that HCT affects a patient physical (e.g., fatigue), psychological (e.g., anxiety and depression symptoms), social (e.g., financial concerns, employment disruptions), and spiritual (e.g., existential concerns) well-being [ 5 ]. HCT recipients may confront fear of death, loss of control, feelings of uncertainty and social isolation, increased dependence, or disabling physical symptoms in the short and long term after transplantation [ 6 , 7 ]. Some models of adaptation and adjustment argue that restoring meaning is central to adapting to these conditions [ 8 ].

Meaning-making process following HCT

The most commonly mentioned factors of meaning reconstruction are meaning-making coping and meanings made [ 1 , 9 ]. Meaning-making is related to the process of searching for meaning and explanation for adversity (i.e., seeking understanding of disease), whereas meanings made is the product of the meaning-making process (i.e., giving meaning to the disease, acceptance, finding benefits, or change of identity due to disease). According to the integrative meaning-making model [ 1 , 10 ], distress related to the discrepancy between global meaning (i.e., basic goals and beliefs, and fundamental assumptions about life) and situational meaning (i.e., the personal significance of a particular situation) initiates meaning-making coping, which impacts the meanings made and then well-being. However, a prolonged unsuccessful search for meaning can be maladaptive. Indeed, the adaptability of meaning-making coping depends on whether the meaning has been found or restored [ 10 ].

A review of the narratives shows that HCT recipients who were able to find meaning in their experience were better able to cope with physical symptoms and were less likely to report unfavorable psychological outcomes after transplant than those who had difficulty finding meaning [ 6 ]. Meanings made was also an essential link connecting meaning-making and well-being in HCT recipients in a daily diary study lasting 28 days after hospital discharge [ 11 ]. The direct effect of average meaning-making coping was unfavorable but positive when mediated by meanings made. In another study among HCT recipients in the late outpatient period with a 4-month follow-up interval, only changes in meaning-making coping were associated with changes in well-being, and these correlates were positive and negative [ 12 ]. The role of meanings made in these relationships was, however, not tested. Indeed, few studies tested the assumptions of the integrative meaning-making model in the context of HCT. More often, the focus is on the global meaning which turns out to be a dynamic construct. In a longitudinal study, sense of meaning decreased 1 month post-HCT and returned to pre-transplant levels by 6 months post-HCT. Moreover, a greater pre-HCT sense of meaning predicted more favorable psychological and physical outcomes during the 12 months following HCT [ 13 ].

Hence, an intervention targeting the ability to successfully search for meaning and find it holds promise in terms of facilitating recovery following HCT and adjustment. To date, no trials tested such interventions among patients undergoing HCT. To the best of our knowledge, two studies are currently underway in HCT recipients that include modules directed at searching for meaning i.e., identifying benefits and meaning. The first one examines the effect of one-on-one, in-person intervention promoting resilience in stress management [ 14 ], whereas the second is a phone-delivered positive psychology intervention [ 15 ]. Both, however, will not evaluate the outcomes from the perspective of the meaning-making model. A systematic review shows that various psychosocial interventions can promote meaning and purpose in the cancer population [ 16 ]. Nevertheless, these targeting meaning enhancements demonstrate a higher effect size. One of the promising approaches potentially fostering meaning-making in disease is Acceptance and Commitment Therapy [ 17 ].

Acceptance and Commitment Therapy (ACT) intervention

Acceptance and Commitment Therapy (ACT) is a transdiagnostic therapeutic approach rooted in the contextual behavioral science that aims to improve the psychological functioning and well-being of individual by increasing psychological flexibility (i.e., the ability to engage in values-based actions even in the presence of unpleasant or difficult experiences) [ 17 ]. To achieve this goal ACT targets six core processes: ( 1 ) contact with the present moment—paying attention to different aspects of the internal and external environment; ( 2 ) self-as-context—the ability to look at one’s internal experiences from a broader perspective; ( 3 ) acceptance—making room for thoughts, feelings, and sensations, even those that are unpleasant; ( 4 ) defusion—noticing thoughts instead of being controlled by them; ( 5 ) values—knowing what really matters; and ( 6 ) committed action—taking values-congruent actions even in the presence of difficulties. During the therapy, the individual learns to assess the workability of strategies used to cope with difficult, unwanted private experiences and to use mindfulness and acceptance skills when necessary. Those skills allow the individual to recognize moments when they have an opportunity to engage in behaviors consistent with their values and fully immerse themselves in those activities, even in the presence of painful thoughts, feelings, or sensations. Individuals are not asked to accept painful private experiences (e.g., physical pain) if there is an effective way to get rid of the pain; acceptance means embracing painful private experiences only when there is no effective way of escaping painful experiences on a long-term basis or when the means of escape comes at too high a cost in terms of valued living. Techniques used in ACT to obtain the aforementioned changes include using metaphors, experiential exercises, and functional analysis [ 17 ].

Besides the typical use of ACT as an individual face-to-face therapy, ACT was also tested in a group format (e.g., for anxiety and depression [ 18 ] or chronic pain [ 19 ]), as a self-help form [ 20 ] as well as technology-supported intervention (using online materials, web or phone applications, telephone) with or without therapeutic guidance [ 21 ].

ACT has been proven to be an effective intervention for various conditions [ 22 ], with the growing number of randomized controlled trials [ 23 ] and mediational studies showing that psychological flexibility is a mediator of the intervention [ 24 ]. Several systematic reviews and metanalyses provide evidence for ACT effectiveness in improving the quality of life and decreasing psychological distress among cancer patients [ 25 , 26 , 27 , 28 , 29 ]. Other systematic reviews support ACT efficacy in improving quality of life and symptoms for long-term chronic conditions [ 30 , 31 ], also including the technology-supported delivery of ACT [ 21 ]. Finally, ACT is considered to be an effective treatment for chronic pain, being recognized by the American Psychological Association as an evidence-based treatment with “strong research support” [ 32 ].

The links between ACT and the meaning-making process

ACT and meaning-making frameworks share common philosophical roots, including constructivism and existentialism [ 9 ]. The ACT model promotes acceptance of what is difficult to change or is not subject to change (such as chronic disease or burden of toxic treatment), taking responsibility for one’s own experiences and actions and creating a meaningful life by engaging in activities that match one’s values [ 33 ]. While meaning-making is not an explicit goal of ACT, creating psychological flexibility should foster meaning-making in disease or following HCT by building more flexible and workable meaning-making explanations of disease [ 34 ]. ACT emphasizes increased awareness of what matters most to the individual and a stepping back from automatic patterns of thought and behavior. Both of these abilities should facilitate meaning-making, i.e., changing global meaning or a reappraisal of situational meaning to achieve congruence, thus alleviating the distress of the event such as HCT. Achieving congruence should end meaning-making coping and be associated with meanings made and improved well-being.

Objectives {7}

This trial aims to examine the effect of an online self-help ACT intervention on the meaning-making process and the underlying mechanisms of change in patients following HCT compared to a minimally enhanced usual care (mEUC) control group. The trial will be enhanced with a single-case experimental design (SCED), where ACT interventions will be compared between individuals with various pre-intervention intervals. As the change process is characterized by complexity, traditional examination of intervention efficacy will be enriched with a temporal perspective (i.e., examination of trajectories of change in primary and secondary outcomes over time) and a systems perspective (i.e., network analysis depicting the pattern of connections between components of the system). The latter assumes that an intervention transforms the connectivity of the networks of intervention goals, the outcome of the intervention, and the connections between the two networks [ 35 , 36 ].

It is hypothesized that the ACT intervention group would show increased psychological flexibility and decreased meaning-related distress compared with the control group (hypothesis 1). Additionally, an increase in meanings made and well-being is anticipated (hypothesis 2). In more exploratory terms, the moderating effect of individual resources (i.e., global and situational meaning, baseline well-being) and demographic and clinical factors on the effect of the intervention will also be examined. Moreover, it is hypothesized that psychological flexibility and meaning-making coping would mediate the ACT intervention effects on meaning-related distress, meanings made, and well-being in HCT recipients (hypothesis 3). Finally, following the network theory, it is hypothesized that the ACT intervention group will display more robust positive connections within the psychological flexibility and meaning-making coping network (hypothesis 4), weaker connections within the distress network (hypothesis 5), more negative connections of distress with psychological flexibility and meaning-making coping (hypothesis 6), and more positive connections between psychological flexibility, meaning-making coping, meanings made, and well-being as compared to control conditions (hypothesis 7).

Trial design {8}

A two-armed parallel randomized controlled trial (RCT) will be conducted to determine the effects of an online Acceptance and Commitment Therapy ACT intervention on the meaning-making process in patients following HCT. Participants will be randomly assigned in a double-blinded manner to ACT intervention and education conditions at a ratio of 1:1. RCT will be enhanced with a randomized multiple-baseline single-case experimental design (SCED). SCED will proceed according to the AB + post-intervention design, where A is the pre-intervention phase and B is the intervention phase, followed by the post-intervention phase. Participants will be randomly assigned to one of three pre-intervention measurement lengths (7 days, 14 days, 21 days) followed by 7-day observations at the 2nd and 3rd post-intervention measure.

Methods: participants, interventions and outcomes

Study setting {9}.

Recruitment will take place in the Department of Bone Marrow Transplantation and Oncohematology of the Maria Sklodowska-Curie National Research Institute of Oncology (MSCNRIO) Gliwice Branch. MSCNRIO branch in Gliwice is the leading facility in Poland that performs HCT. Approximately 150 primary transplants are performed there annually (approx. 200 HCT in total).

Eligibility criteria {10}

The participation criteria will include ( a ) qualification for the first autologous or allogeneic HCT due to hematologic malignancies or solid tumors, ( b ) age ≥ 18 years, ( c ) signed written informed consent, ( d ) ability to read and write in Polish, and ( e ) daily access to the Internet by computer and/or mobile device. The exclusion criteria will be as follows: ( a ) major psychiatric or cognitive disorder that would impede providing informed consent and study participation, ( b ) inability to cooperate and give informed consent, ( c ) hearing, seeing, or movement impairment that precludes participation, ( d ) current participation in any form of psychotherapy, ( e ) no access to the Internet and computer and/or mobile device, and ( f ) inability to use a computer and/or mobile device and the Internet.

Who will take informed consent? {26a}

Written informed consent to participate in the study will be obtained by the recruiter (member of the research team), in direct contact with the participant and after an extensive briefing.

Additional consent provisions for collection and use of participant data and biological specimens {26b}

N/A. Biological specimens will not be collected.

Interventions

Explanation for the choice of comparators {6b}.

In RCT, the ACT intervention will be compared with minimally enhanced usual care (mEUC). Standard psychological care following HCT does not include a standard psychological care protocol. Psychological care for HCT recipients is provided if needed according to the physician’s recommendation in the event of the patient’s functioning deteriorating. Thus, to maintain the same conditions in both trials, participants in the control condition will receive cognitively neutral tasks (education) from which no effects are expected for the meaning-making process. In SCED, comparisons between participants with different pre-intervention measurement lengths will be conducted.

Intervention description {11a}

ACT intervention “The Path to Health” will start on the second day after hospital discharge for individuals in RCT or after 7–21-day pre-intervention measurement in individuals in SCED. It will take 14 days (+ day 0 with organizational information). Each day, participants will receive a web-based intervention consisting of the theoretical introduction (including examples of patients’ experiences and metaphors) and practical ACT activity (e.g., reflective questions, experiential exercise, values card sorting test). Most of the activities are followed by a debrief that includes the patient’s reactions to this particular exercise and practical tips. On some days, participants will also receive additional exercise (optional).

Using the metaphor of life as a journey, participants will learn to recognize where they are headed (values), when there is a moment of choice between actions that lead towards values or away from them, and how to use attention flexibly to free themselves from the power of thoughts, to open up and accept emotions so that they can effectively take action in line with their values (Table  1 ). Each introduction and each activity will be available in written form and audio. The ACT intervention is built from standard ACT activities [ 37 , 38 , 39 , 40 ] and tailored to the context of the disease and treatment. Participants will be advised to do one activity a day, but they will be able to come back to the chosen activities or practice them a couple of times if necessary.

During the same period, participants allocated to the education in RCT will receive an online guide to post-HCT recommendations. Each day, participants will receive information about post-transplant prescriptions along with exercises. Participants will receive guidelines in several areas: diet, physical activity, hygiene, rest, social interactions, and sexual health. During the first 3 days, nutrition will be discussed, including the principles of healthy diet after HCT. On the fourth day, participants will learn the rules of personal hygiene. The fifth day is devoted to presenting the rules aimed at preventing infection. On the sixth day, the issue of body fatigue will be discussed. For the next 3 days, the main topic will be the resumption of activity, mostly physical activity. The tenth day is devoted to safe social contacts. On the eleventh day, participants will work on their sleep. On the twelfth day, sexual health will be discussed. Day 13 is devoted to discussing the issue of rest. And the last day will be a summary of all the guidelines. The exercises serve as an extension of the topic (e.g., watching a video presenting the principles of nutrition) or the emphasis is on practice to support the implementation (e.g., preparing a sequence of exercises and performing them several times a day). The content is prepared based on available guides for HCT recipients. It was also verified by a hemato-oncologist.

Criteria for discontinuing or modifying allocated interventions {11b}

Modification of assigned interventions is not provided for. Disease recurrence will be the criteria for discontinuation of the intervention. The participant can also discontinue the intervention at any time without any negative consequences.

Strategies to improve adherence to interventions {11c}

To improve adherence to the intervention, participants will receive daily reminders about the intervention. Also, direct technical support will be available 24/7. If participants drop out or stop using the intervention, they will be asked for the reason(s) why they decided to quit the intervention and/or study.

Relevant concomitant care permitted or prohibited during the trial {11d}

Individuals participating in any form of psychotherapy will not be eligible for the study. Participation in forms of psychological support will be monitored on an ongoing basis.

Provisions for post-trial care {30}

Upon completion of the study, all participants will have access to the self-help ACT intervention booklet with written and recorded exercises.

Outcomes {12}

The primary and secondary outcomes will be assessed at baseline (before HCT), during the intervention, immediately, 1 month, and 3 months after the intervention (Table  2 ). In SCED, 1 month and 3 months post-intervention assessments will be preceded by 7-day daily diaries. A summary of the outcome measures that will be used in this study is available in Table  3 .

Primary outcomes

The primary outcome will be the changes compared to the baseline in meaning-related distress as assessed by the Global Meaning Violation Scale (GMVS) [ 41 ].

Secondary outcomes

The secondary outcomes will be changes from baseline in global meaning, situational meaning, meanings made, and well-being. Global meaning will be measured by cognitive and emotional representations of illness and global presence of meaning using the Brief-Illness Perception Questionnaire (B-IBP) [ 42 ] and Meaning in Life Questionnaire (MLQ) [ 43 ], respectively. Coping self-efficacy, an indicator of situational meaning, will be assessed with the Perceived Coping Self-Efficacy (CSE) Scale [ 44 ]. Meanings made will be assessed using the “current standing” Post-Traumatic Growth Inventory-Short Form (C-PTGI-SF) [ 45 , 46 ] and 3-item scale based on the Meaning of Loss Codebook (MLC) [ 47 ]. Depressive and anxiety symptoms will be assessed with the Patient Health Questionnaire (PHQ-4) [ 48 ], while loneliness, as recommended by the British Office for National Statistics [ 49 ], will be evaluated with the enhanced R-UCLA 3-item Loneliness Scale [ 50 ] and direct question from the Community Life Survey [ 51 ].

Mediators and moderators

To assess putative mechanisms of change and change moderators, meaning-making coping and psychological flexibility will be measured longitudinally. In this scheme, deliberate and automatic meaning-making coping will be assessed with the Core Beliefs Inventory (CBI) [ 52 ] and the intrusive ruminations subscale from the Event-Related Rumination Inventory (ERRI) [ 53 ], respectively. Psychological flexibility will be measured using the Comprehensive Assessment of Acceptance and Commitment Therapy Processes (CompACT-9) [ 54 ]. In addition, fluctuations in meaning-making coping, meanings made, psychological flexibility, and well-being (i.e., subjective health and positive and negative affect) will be measured in an intensive longitudinal manner (i.e., daily) throughout the intervention in RCT and pre- to post-intervention in SCED. Daily meaning-making coping (deliberate and automatic) will be measured with an abbreviated and tailored to the daily measurement and context of the study 4-item version of the ERRI questionnaire. Daily meanings made will be evaluated using a contextualized 3-item scale based on the Meaning of Loss Codebook (MLC). Daily psychological flexibility will be measured using a shortened to 4-item version of the CompACT questionnaire. Daily subjective health will be assessed by a single-item statement “Generally, I can say my health today was…” on a 5-point scale ranging from 1 (bad) to 5 (excellent). Daily positive and negative affect will be assessed with two positive (happy, cheerful) and two negative adjectives (sad, gloomy) based on the Circumplex Model of Emotion [ 55 ].

Feasibility will be examined via attrition and adherence rates as well as questions about intervention engagement. Acceptability will be measured by intervention satisfaction and evaluation (attractiveness and easiness). Adherence to the intervention will be estimated based on the dropout rate (i.e., the percentage of participants who do not log in to the intervention on a given day) and self-reported questions about engagement in the intervention: ( 1 ) the number of days on which the proposed exercises were done seriously, ( 2 ) the number of minutes spent on average in training, and ( 3 ) the use of various training components. Satisfaction with the intervention will be measured using 4 questions (no. 3, 4, 7, and 8) from the Client Satisfaction Questionnaire (CSQ-8) [ 56 ] modified to the intervention context and online form. Evaluation of the intervention will be assessed using questions of the author’s own measuring the ease and attractiveness of the training.

The cost-effectiveness of the intervention will be examined by estimating health-related quality of life as measured by the Quality of Life Questionnaire of the European Organization for Research and Treatment of Cancer (EORTC QLQ-C30) [ 57 ].

Other measures

At the baseline, demographic data (e.g., age, sex, education, marital status, employment) will also be collected and partially measured using the Diversity Minimal Item Set (DiMIS) [ 58 ]. Clinical data (e.g., diagnosis, time since diagnosis, conditioning, concomitant diseases) will be obtained from the medical records.

Participant timeline {13}

Figure  1 describes the project timeline.

Timeline for RCT and SCED study

Sample size {14}

In RCT, the sample size was calculated based on an analysis of variance with two groups (ACT versus mEUC) and four repeated measures of variance (ANOVA) with within-between interaction (group x time) using the G*Power calculator [ 59 ] and simulation study of the time course with dichotomous between-person level predictor [ 60 ]. Given the large effects of ACT on psychological well-being, including hope (Hedge’s g  = 0.88–2.17) and medium effects on psychological flexibility among cancer patients (Hedge’s g  = 0.58) [ 29 ], the stronger effects in the population of women with breast cancer compared to patients with other types of cancer (large versus medium effect sizes) [ 31 ], and medium effect sizes of technology-supported ACT interventions (Hedges’ g  = 0.44–0.48) [ 21 ], moderate differences between conditions were expected. Assuming a medium effect size of f  = 0.25, a power of 0.80, and an alpha level of 0.05 in repeated measures of ANOVA, a total sample size of N  = 178 is required. In turn, on the basis of a simulation study, a total sample size of N  = 136 is required for multilevel modeling. Therefore, the minimum sample size was assumed of N  = 160 (80 per condition). Allowing for the potential attrition rate of 20%, this leads to a sample size of N  = 192 participants, including 96 in each arm. In SCED, 6–9 participants will be investigated, a minimum of 2 per condition. According to the simulation study [ 61 ], sufficient power (0.80) can be reached in SCED with six to eight participants, depending on the assumed effect size (large versus medium, respectively).

Recruitment {15}

Recruitment will take place at a single center, after elective admission to the bone marrow transplantation and oncohematology unit due to HCT before the start of conditioning treatment. Recruitment will take place on average on the 2nd day after admission. Every 2 days, the transplant coordinator, PI, and physician (members of the research team) will review the lists of patients enrolled for HCT. Those who meet the inclusion criteria will be initially informed of the purpose of the study and invited for an extensive briefing by a recruiter (member of the research team). Patients will also be allowed to ask any remaining questions about the aim of the study and the study procedures. After receiving an extensive briefing, all patients who give written informed consent will proceed with baseline. Recruitment will be carried out until the desired sample size is achieved. The flowchart of the study is depicted in Fig.  2 .

Participant flowchart in RCT and SCED study. ACT, Acceptance and Commitment Therapy; mEUC, minimally enhanced usual care

Assignment of interventions: allocation

Sequence generation {16a}.

The allocation sequence will be generated using the method of minimization. Minimization can be classified as dynamic allocation or covariate adaptive methods because the allocation depends on the characteristics of the patients and is performed continuously [ 62 ]. Randomization will be stratified by type of transplant (autologous versus allogeneic) to ensure a balanced representation between the study conditions because autologous and allogeneic HCT recipients experience different recovery trajectories and HCT impact on well-being [ 63 , 64 ].

Concealment mechanism {16b}

The mechanism of implementing the allocation sequence will be central randomization. It means generating an allocation sequence after the patient is enrolled [ 65 ]. This way, randomization will not affect the recruitment process.

Implementation {16c}

The trial coordinator (member of the research team) will enroll participants, generate the allocation sequence, and assign participants to interventions. Other members of the team will be blind to the allocation of the participants to the conditions.

Assignment of interventions: blinding

Who will be blinded {17a}.

In RCT, trial participants, care providers, outcome assessors, and data analysts will be blinded after assignment to interventions. Blinding will be performed using two separate databases: one containing participant allocation information (blinded) and the other containing the remaining information (unblinded). Only the trial coordinator will have access to the blinded database.

Procedure for unblinding if needed {17b}

Disclosure of the participant allocation will take place after the completion of the study and analysis of the first results examining the efficacy of the online ACT intervention.

Data collection and management

Plans for assessment and collection of outcomes {18a}.

Data will be collected via self-reported online questionnaires at the baseline (before HCT), post-intervention, and 1 and 3-month follow-ups (Table  2 ). In addition, to assess momentary changes and mechanisms of change, participants will complete daily diaries throughout the intervention. SCED participants will complete 7-day daily diaries repeatedly, i.e., before 1 and 3-month follow-ups. The detailed characteristics of the study instruments are presented in Table  3 .

We intend to collect clinical data (e.g., diagnosis, time from diagnosis, type of transplant and conditioning treatment, comorbidities) from the patient’s medical records. The participants will give their additional consent for the data to be collected from their medical history by a physician (team member). If the participant does not approve of access to the data from medical records, they will be requested to provide information themselves.

Plans to promote participant retention and complete follow-up {18b}

To improve participant retention and complete follow-up, participants will receive email and phone reminders about the survey and subsequent measurements. If participants fail to complete study assessments, motivational reminders will be sent repeatedly by email. In daily diary measurements, participants who give written consent will receive SMS reminders. Since the daily diaries will not be filled retrospectively, a single reminder with the mailing of the survey will be used.

During the study, direct technical support will be available 24/7, and a research team member will contact the participant by phone to resolve any issues and answer questions. If participants drop out of the study, they will be asked for the reason(s). Any other attritions (e.g., disqualification from HCT, death) along with the reasons will be recorded.

Data management {19}

Questionnaire data collection will be done electronically (using the SurveyMonkey platform, which encrypts and secures data during transit and the data stored; the accounts are password-protected with available complexity controls). Medical data will be collected electronically directly from the medical records registry by the physician (member of the research team). Only informed consents will be paper documents, collected and entered by recruiter (member of the research team). The PI will be responsible for the secure delivery of the documents to the trial office. The PI and trial coordinator will oversee the quality of the data. Data and metadata storage will take place in the university’s central resources according to the 3–2-1 rule. The detailed data management plan is available at OSF .

Confidentiality {27}

Personal data such as phone numbers and email addresses of the participants will be encrypted (using individual trial identification number) and stored only during the data collection period. Written informed consent and the data identifying the participants will be stored separately under lock and key and will be kept strictly confidential. The data will be accessed by the PI of the project and selected team members who will be contacting the participants (trained in the General Data Protection Regulation). Access to the data will be monitored and possible only after obtaining the access rights that the PI of the project will grant. Once data collection is completed, the data will be anonymized and in this form will be analyzed statistically.

Plans for collection, laboratory evaluation and storage of biological specimens for genetic or molecular analysis in this trial/future use {33}

N/a. Biological specimens will not be collected.

Statistical methods

Statistical methods for primary and secondary outcomes {20a}.

Analyses will be conducted using the latest Mplus statistical package [ 66 ], R [ 67 ], and IBM SPSS (IBM Corp.; Armonk, NY). We will use the standard α  = 0.05 or 95% confidence interval for the determination of value probability. All data analysis will be performed according to the intention-to-treat principle, where all randomized participants are included in the analysis assuming missing data at random. The collected data will be first analyzed in terms of sample characteristics and comparisons (frequency, descriptive statistics; ANOVA, t -test or their nonparametric counterparts; χ 2 ; Pearson’s or Kendall’s correlation), missing data (frequency, multilevel modeling), and sample attrition (logistic regression analysis). Multilevel confirmatory factor analysis (MCFA) will be performed to establish the respective measurement models and calculate the indicator reliabilities (omega coefficient) at the within- and between-person levels [ 60 , 68 ]. To examine hypotheses 1–3, latent curve growth modeling (LCGM) [ 69 ] and multilevel (MSEM) and dynamic structural equation modeling (DSEM) will be applied [ 60 , 70 ]. All methods allow for the examination of the time course. In addition, MSEM and DSEM allow for the calculation of simple between- and within-person associations and more advanced associations such as mediations and moderations. Hypotheses 4–7 will be verified using a multilevel vector autoregressive (mlVAR) model [ 71 ]. mlVAR allows for the examination of a temporal network (i.e., lagged predictive relations between each node in the network and each node in the network at the next measurement occasion), a contemporaneous network (i.e., partial correlations within the same measurement occasion), and a between-person network (i.e., associations between nodes that are averaged across measurement occasion).

Interim analyses {21b}

Due to a known minimal risk, i.e., testing interventions with known positive effects, an interim analysis plan was not created. The principal investigator (PI) will make the final decision to terminate the study once the optimal number of study participants has been obtained.

Methods for additional analyses (e.g., subgroup analyses) {20b}

All analyses will be supplemented by sensitivity analyses. In all models, possible confounders (i.e., demographics, clinical factors, and other confounders) will be considered after preliminary selection.

Methods in analysis to handle protocol non-adherence and any statistical methods to handle missing data {20c}

The statistical methods used (i.e., MSEM, DSEM) will allow the most recent flexible approach to the missing data (the full information maximum likelihood) [ 72 , 73 ]. In less sophisticated analyses, missing data will be multiple imputed in advance.

Plans to give access to the full protocol, participant-level data and statistical code {31c}

The full protocol, dataset, statistical codes, and outputs will be made available at the Open Science Framework (OSF). Participant-level datasets will be publicly available, however without demographics and clinical data due to privacy or ethical restrictions (the possibility of identification of participants).

Oversight and monitoring

Composition of the coordinating center and trial steering committee {5d}.

The study’s coordinating center is SWPS University. The study’s steering committee will consist of a health psychologist, a certified cognitive behavioral therapist (CBT) and ACT therapist, and a doctoral student (master’s degree in psychology). The committee’s responsibilities will be to develop the intervention and then implement it and monitor implementation. The committee will meet 2–4 times a month.

Composition of the data monitoring committee, its role and reporting structure {21a}

Due to known minimal risks, a formal committee of data monitoring is not needed.

Adverse event reporting and harms {22}

In this study, an adverse event will be defined as any deterioration in mood that requires specialized treatment, collected after the individual has received the intervention, and reported to the local institutional review board (IRB).

Frequency and plans for auditing trial conduct {23}

No audit procedures are planned. An independent audit may be conducted by the local IRB and the sponsor.

Plans for communicating important protocol amendments to relevant parties (e.g., trial participants, ethical committees) {25}

Communication of significant protocol modifications and study outcomes will be done to the funder, the ethics committee, and the public through ClinicalTrials.gov.

Dissemination plans {31a}

The results will be published in peer-reviewed journals and presented at thematic international scientific conferences. Also, during the debriefing, participants will be informed of the web address of the project website, where a lay summary of the study updated with the results (when available) will be posted.

Effective treatment of patients undergoing HCT likely requires a focus also on those mechanisms that support the reconstruction of meaning damaged by medical treatment and the disease itself. An intervention based on ACT, an empirically validated theoretical model [ 17 ], appears to be a promising psychological therapy to support the reconstruction of meanings [ 33 , 34 ]. This trial represents the first study that aims to integrate the ACT and meaning-making frameworks to reduce meaning-related distress, stimulate the meaning-making process, and enhance the well-being of HCT recipients. It builds on previous successful ACT interventions that strengthened cancer patient well-being albeit outside the context of meaning reconstruction [ 25 , 26 , 27 , 28 , 29 ]. Moreover, testing a specific theory-based intervention to address existential concerns unique to patients undergoing HCT will be reinforced by a statistically rigorous idiographic approach. SCED will allow us to go beyond aggregate group effects and see how a specific person responds to an ACT intervention, thereby providing clinical input into what works for whom and when . Beyond this, since access to interventions in the HCT population is limited, the web-based ACT self-help program we designed has the potential to fill that gap. Self-directed ACT interventions are considered cost-effective, flexible, and accessible for cancer patients [ 21 ]. They allow patients to self-determine what (content), when (time), where (location), and how (read or listen) to use ACT intervention booklets.

Despite these strengths, we expect several challenges and limitations. First, recruiting the HCT recipients will be challenging. Therefore, we allow for the possibility of recruiting at a second oncohematology center with identical credentials. Retaining participants in the study can be also a challenge, hence the contact maintenance and participation reminder activities we have planned. In addition, we plan to compensate participants for their participation at a rate of PLN 150 (approx. 34.5 Euros) in RCT and PLN 300 (approx. 69 Euros) in SCED. Another limitation is the targeting of the trial to all willing HCT recipients, regardless of the level of distress or the stage of the meaning reconstruction process. However, we are guided by pragmatic (restrictive inclusion/exclusion criteria would prolong the already long data collection time) and cognitive considerations (to our knowledge, this is the first study that will test the relationship of ACT interventions to meaning reconstruction processes) hoping that this will result in further research in this area.

Trial status

ClinicalTrials.gov, NCT06266182. Registered 20 February 2024, https://clinicaltrials.gov/study/NCT06266182 . Version 3.0 dated May 13, 2024. Patient recruitment began on March 6, 2024. Recruitment is expected to be completed in December 2025.

Availability of data and materials {29}

Data that will be collected during the current study (without demographics and clinical data due to the possibility of identification of participants), full protocol, statistical codes, and outputs will be made available at the Open Science Framework (OSF).

Abbreviations

• Acceptance and Commitment Therapy

Analysis of variance

Brief-Illness Perception Questionnaire

Core Beliefs Inventory

Cognitive behavioral therapy

Comprehensive Assessment of Acceptance and Commitment Therapy Processes

The “current standing” Post-Traumatic Growth Inventory-Short Form

Coping Self-Efficacy Scale

Client Satisfaction Questionnaire

Diversity Minimal Item Set

Dynamic structural equation modeling

Quality of Life Questionnaire of the European Organization for Research and Treatment of Cancer

Event-Related Rumination Inventory

Global Meaning Violation Scale

• Hematopoietic cell transplantation

Institutional review board

Latent curve growth modeling

Multilevel confirmatory factor analysis

Minimally enhanced usual care

Meaning of Loss Codebook

Meaning in Life Questionnaire

Multilevel vector autoregressive

Maria Sklodowska-Curie National Research Institute of Oncology

Multilevel structural equation modeling

Open Science Framework

Patient Health Questionnaire

Principal investigator

• Randomized controlled trial

Revised UCLA Loneliness Scale

• Single-case experimental design

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Acknowledgements

Not applicable.

The work is supported by the National Science Centre, Poland [grant number 2020/39/B/HS6/01927 awarded to AK]. The funders had no role in the study design, data collection, analysis, and interpretation, decision to publish, or preparation of the manuscript.

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Aleksandra Kroemeke & Marta Kijowska

Faculty of Psychology, SWPS University, Warsaw, Poland

Joanna Dudek

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Department of Bone Marrow Transplantation and Oncohematology, Maria Sklodowska-Curie National Research Institute of Oncology Gliwice Branch, Gliwice, Poland

Małgorzata Sobczyk-Kruszelnicka

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Contributions

AK is a principal investigator, who led the proposal and protocol development. JD developed the ACT intervention and contributed to the study design. MK developed cognitively neutral tasks (education) for the control group and assisted in the development of the ACT intervention. RO offered review and advice on ACT intervention component. MSK reviewed the manuscript. AK, MK, and MSK will be involved in the recruitment of participants and data collection. AK, JD, and MK drafted the manuscript. All authors have approved the manuscript.

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Correspondence to Aleksandra Kroemeke .

Ethics declarations

Ethics approval and consent to participate {24}.

The study has been reviewed and approved by the Ethical Review Board at SWPS University, Faculty of Psychology in Warsaw (Decision No. 52/2023 of December 12, 2023), and adheres to the ethical guidelines of the Declaration of Helsinki. All participants will be requested to give written informed consent before participation (assessment and randomization).

Consent for publication {32}

Not applicable—no identifying images or other personal or clinical details of participants are presented here or will be presented in reports of the trial results. The participant information materials and informed consent form are available from the authors on request.

Competing interests {28}

The authors declare that they have no competing interests.

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Kroemeke, A., Dudek, J., Kijowska, M. et al. The effect of an online acceptance and commitment intervention on the meaning-making process in cancer patients following hematopoietic cell transplantation: study protocol for a randomized controlled trial enhanced with single-case experimental design. Trials 25 , 392 (2024). https://doi.org/10.1186/s13063-024-08235-1

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• Minyan Wang ,
• Haojie Ni ,
• Chu Qin and
• http://orcid.org/0000-0002-8329-8927 Conghua Ji
• Zhejiang Chinese Medical University , Hangzhou , Zhejiang , China
• Correspondence to Professor Conghua Ji, Zhejiang Chinese Medical University, Hangzhou, Zhejiang 310053, China; jchi2005{at}126.com

Although randomised controlled trials are considered the gold standard in clinical research, they are not always feasible due to limitations in the study population, challenges in obtaining evidence, high costs and ethical considerations. As a result, single-arm trial designs have emerged as one of the methods to address these issues. Single-arm trials are commonly applied to study advanced-stage cancer, rare diseases, emerging infectious diseases, new treatment methods and medical devices. Single-arm trials have certain ethical advantages over randomised controlled trials, such as providing equitable treatment, respecting patient preferences, addressing rare diseases and timely management of adverse events. While single-arm trials do not adhere to the principles of randomisation and blinding in terms of scientific rigour, they still incorporate principles of control, balance and replication, making the design scientifically reasonable. Compared with randomised controlled trials, single-arm trials require fewer sample sizes and have shorter trial durations, which can help save costs. Compared with cohort studies, single-arm trials involve intervention measures and reduce external interference, resulting in higher levels of evidence. However, single-arm trials also have limitations. Without a parallel control group, there may be biases in interpreting the results. In addition, single-arm trials cannot meet the requirements of randomisation and blinding, thereby limiting their evidence capacity compared with randomised controlled trials. Therefore, researchers consider using single-arm trials as a trial design method only when randomised controlled trials are not feasible.

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https://doi.org/10.1136/spcare-2024-004984

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WHAT IS ALREADY KNOWN ON THIS TOPIC

Single-arm trials refer to a design method in which only one experimental group is established, without a control group. And, more and more studies have adopted the single-arm test design.

WHAT THIS STUDY ADDS

In some cases, single-arm trials have certain ethical advantages over randomised controlled trials, but researchers need to be careful to remain strictly scientific. Single-arm trial satisfies the principle of control, repetition and balance in design.

HOW THIS STUDY MIGHT AFFECT RESEARCH, PRACTICE OR POLICY

In clinical practice, for refractory diseases and rare diseases, suitable treatment schemes can be found through single-arm trial. In terms of study design, when randomised controlled trials are not feasible, single-arm trial design can be used as one of the alternative methods.

Introduction

Careful trial design is key in clinical research. A good trial design leads to the successful implementation of a clinical trial and the production of clear results. 1 The high-quality evidence sought during clinical trials is often achieved through randomised controlled trials (RCTs), 2 which have long been regarded as the gold standard for evidence generation in the medical field because they provide a fair and accurate assessment of the effectiveness of treatments without the influence of confounding factors. 3 Ideally, medical treatment should be subjected to rigorous large-sample RCTs. However, limitations associated with study populations, challenges in obtaining evidence, high costs and ethical considerations hinder this, making RCTs infeasible in some cases. For example, there are still more than 30 000 ongoing clinical studies in the field of cardiovascular disease that face challenges, such as difficulties recruiting patients, resulting in delays in their completion or timely publication. 4 Traditional trial designs must be adapted to the current needs of rapidly evolving genomics, immunology and precision medicine. 5 Consequently, an increasing number of innovative trial designs, such as single-arm trials, 6 cluster randomised trials 7 and adaptive trials, 8 have been developed.

Single-arm trials refer to a design method in clinical research where only one experimental group is established, without the inclusion of a parallel control group. 9 It can be considered as an alternative when the design of an RCT is not feasible. The study design is open and does not involve randomisation or blinding. This type of experimental design is mostly used in the early stages of drug research, especially in the field of antitumoural therapy, for several critical illnesses, rare diseases and diseases for which no treatments are currently effective. In recent years, more and more single-arm trials have been applied to clinical research, 10 11 and relevant departments have also added single-arm trial design to new drug research guidelines. 9 12 These guidelines and standards aim for standardisation and consistency in single-arm trials to improve their quality and reliability.

Single-arm trials meet ethical requirements more easily and require lower sample sizes, lower trial costs and shorter trial times than RCTs. However, owing to the lack of parallel control groups, many confounding factors are difficult to control, and the conclusions of the trials may be difficult to interpret and are only used for evidence and decision-making when the effect size is clinically significant. Currently, single-arm trials are mainly used for the initial exploration of clinical trials for tumours, rare diseases, significant effects and high-demand drugs. 13 14

This article mainly analyses the advantages and disadvantages of single-arm trials in terms of scientific and ethical considerations in clinical research and provides reference suggestions for their application.

Overview of the study design

Clinical trial staging.

Single-arm trials are a commonly used clinical trial design that can be applied in all four phases of clinical trials. In the phase I clinical trials, single-arm trials are employed to investigate the mechanism of action, pharmacokinetic properties and safety of a new drug, providing foundational data for subsequent clinical trials. 15 The phase II trials aim to evaluate the efficacy and preliminary safety of a treatment and provide evidence for proceeding to a phase III trial. 16 Phase III trials typically involve large-scale RCTs designed to provide sufficient evidence to support the efficacy and safety of a new drug or treatment method. 17 However, due to ethical limitations and challenges in patient recruitment, 18 single-arm trial designs are also used in phases II and III clinical research. Guidelines and regulations pertaining to single-arm trials are continuously evolving, 10 11 particularly in phase II trials, as they can yield faster results, saving time and costs. Phase IV trials, also known as postmarketing studies, are conducted to monitor and assess the long-term effectiveness and safety of a drug, as well as explore new indications. In certain cases, single-arm trial designs have also been employed in phase IV trials.

Application scenarios

The wide variety of disease areas covered by the application of single-arm trial designs include oncological, 19 circulatory, immune, 20 haematological 21 and infectious 22 diseases among others. Most interventions studied in single-arm trials are pharmacological interventions and new therapeutic regimens, such as targeted therapy, gene therapy or multidrug combinations. Other types of interventions include surgery, 23 minimally invasive radiofrequency therapy 24 and the use of medical devices. 25 In addition, single-arm trials are also applied in rare diseases, new drug research, adverse reaction monitoring and other areas.

Oncological diseases

In oncology, single-arm trials are used to design protocols for treating refractory, recurrent and metastatic cancers. These conditions are usually very severe, and the patients have a short survival period; therefore, new and more effective treatments are needed. Owing to the lack of effective treatments, single-arm trials have become an important method for these patients to gain access to new drugs. Over recent years, an increasing number of findings from single-arm trials have been used to support the introduction of new drugs to the market. For example, by 31 December 2020, 125 of the 254 new drug studies approved by the US. Food and Drug Administration’s Accelerated Approval Programme were single-arm trials, representing 49% of the total, 26 while 11 of the 54 clinical trials on antineoplastic drugs approved in Europe between 2014 and 2016 were single-arm trials. 27 In a study on refractory thymic carcinoma, Sato et al conducted an efficacy analysis of a therapeutic drug using an external control single-arm trial design. 28

Obtaining approval for large-scale RCTs in patients with advanced cancer can be ethically challenging because of the potential for additional suffering and risk to patients. 29 30 Therefore, when RCTs are not feasible, single-arm trials become one of the solutions.

Rare diseases

Rare diseases are highly specific and involve a relatively small number of patients, making it difficult to find a sufficient number of control participants for the study. 31 Owing to the scarcity of patients, conducting controlled trials and recruiting patients becomes exceptionally difficult. 32 In such cases, finding a sufficient number of patients and control participants tends to be time-consuming and costly. However, the single-arm trial design does not include a parallel control group and only involves treating patients, conducting follow-up and analysing the data. 32 Thus, single-arm trials are more suitable for rare disease research because of their smaller sample size while aiding in understanding the pathogenesis, pathophysiological characteristics and treatment and prevention of rare diseases. For example, Wagner et al analysed the therapeutic efficacy of malignant perivascular epithelioid cell tumour through self-controlled single-arm trial. 33 Using a single-arm trial allows all participants to receive the intervention under investigation and also enhances patients’ willingness and satisfaction to participate in the trial, thus facilitating the smooth progress of the research.

Outbreaks of infectious diseases

Treatment selection is crucial during sudden outbreaks of infectious diseases. RCTs, although more scientifically sound, require longer research cycles to identify effective treatments and single-arm trials with shorter research cycles have become an important option to identify treatments as quickly as possible for diseases characterised by rapid spread, widespread impact and high severity. 34 35 In addition, single-arm trials are more advantageous given the willingness and level of participation of the patients. Many patients are willing to participate in trials and try new treatments because of the urgency and severity of their condition, and their active participation provides strong support for the research. For example, for COVID-19 outbreak, the protocols of single-arm trials were rapidly developed and adopted to find effective treatment options as quickly as possible. 34 36 Significant results were obtained from these trials within a short period, and valuable references for clinical treatment were obtained. These results helped to ensure better treatment for patients with COVID-19 infection at that time and provided important experience and support for future responses to similar outbreaks.

New treatment programmes

Diseases for which no effective treatment has been developed and for which a gold standard treatment is yet to be established are also suitable for single-arm trials. This approach has an important role in clinical research, particularly in the exploratory studies of rare or novel diseases. 37 Researchers can use single-arm trials to evaluate the effectiveness of new treatment strategies or drugs, addressing the challenges encountered in patient recruitment and facilitating the timely identification of suitable treatment regimens or drugs. The single-arm trial design can provide scientific evidence in specific circumstances for diseases where a definitive treatment is lacking. Cheng et al conducted a study on a new treatment approach for psoriasis using a single-arm trial. 38

Medical equipment

Single-arm trials are invaluable in medical device-related research, particularly in areas requiring surgical intervention. This trial design provides physicians with a convenient way to evaluate the safety and efficacy of new medical devices, thereby helping them to choose better treatment options. 39 40 For tricuspid regurgitation symptoms, Nickenig et al designed a single-arm trial to demonstrate the efficacy of the TriClip system. 41 In some cases, single-arm trials are viable. For example, in medical device-related studies, RCTs may not be applicable because of ethical or safety concerns.

Ethical principle embodied in the single-arm trials

Ethical principles.

To ensure that the trial complies with ethical principles and protects the rights of participants, several ethical requirements need to be met during the design and conduct of single-arm trials. These requirements include:

Informed consent: Like any other clinical trial, a single-arm trial requires obtaining informed consent from participants. Researchers must provide comprehensive trial information, including the purpose of the trial, intervention measures, potential risks and benefits, and any available alternative treatments or choices. The process of obtaining informed consent should adhere to ethical guidelines and ensure that participants understand the nature of the trial and its potential consequences.

Balancing risks and benefits: Since single-arm trials inherently lack a control group for comparison, researchers must carefully assess and inform patients about the potential risks associated with the trial intervention, ensuring their full understanding. During trial design, potential benefits and possible adverse effects should be carefully weighed, and efforts should be made to ensure that the potential benefits of the intervention outweigh the risks that participants may face.

Participant safety: Protecting the safety of participants during the trial is of utmost importance. Appropriate safety measures and monitoring protocols should be implemented to minimise potential harm. Regular assessments of participants’ physical conditions should be conducted, and any potential adverse events should be promptly addressed.

Data collection and analysis: Scientific rigour and transparency should be followed during data collection and analysis. Researchers should adhere to standardised protocols and ensure transparency in reporting results. This helps accurately interpret the trial results and facilitates evidence-based decision-making.

Ethical review and oversight: Similar to any other clinical trial, single-arm trials also require ethical review and oversight by research ethics committees or institutional review boards. These entities evaluate the trial design, informed consent process, participant safety measures and overall ethical considerations to ensure that the trial meets ethical standards.

Ethical advantages

Compared with RCTs, single-arm trials have certain ethical advantages in some situations:

Equity in treatment: In a single-arm trial, all participants receive the experimental intervention, eliminating the potential disparity that arises from randomisation. This ensures that every participant has an equal opportunity to receive the treatment being investigated, which is particularly important when the control group receives a placebo or standard treatment. However, it is important to note that patients in single-arm trials also face similar potential risks.

Respect for patient choice: Single-arm trials provide an option for patients who do not wish to be assigned to a control group receiving a placebo or standard treatment. It respects patients’ autonomy by allowing them to access the experimental intervention without being randomised to a non-intervention group.

Opportunity for access to new treatments: Single-arm trials offer patients the opportunity to access new treatment methods or interventions that may not be available outside of the trial. This is particularly important in the case of rare diseases or limited treatment options. It allows patients to potentially benefit from innovative therapies, improving their quality of life or even providing life-saving benefits.

Feasibility in rare diseases: Conducting RCTs in rare diseases can be challenging due to the limited number of eligible patients. Single-arm trials require smaller sample sizes, making them more feasible in such cases. By using a single-arm design, researchers can gather important preliminary data on the effectiveness and safety of the intervention, which can inform future research and treatment decisions.

Ethical considerations in control group use: In some cases, using a control group in an RCT may raise ethical concerns. For example, if an existing treatment has already been proven highly effective, it may be considered unethical to assign participants to a control group and deny them the known treatment. In such cases, single-arm trials can provide an ethical alternative by evaluating the effectiveness of the intervention without compromising the ethical principles of patient care.

Timely handling of adverse events: Single-arm trials are non-blinded trials, allowing researchers to provide better follow-up and monitor participants’ physical conditions. If adverse events occur, researchers can promptly provide relevant treatment, saving unblinding time and avoiding irreversible consequences.

It is important to consider these ethical advantages in the context of each specific study and balance them with scientific rigour to ensure the validity and ethical integrity of the research.

Scientific principles embodied in the single-arm trials

A single-arm trial is a unique research design that cannot fully realise the principles of randomisation and blinding. Therefore, the study design must follow the principles of control, replication and equilibrium as much as possible to ensure accuracy and reliability. This paper summarises the different ways that RCTs and single-arm trials meet the scientific principle.

Principle of control

Although a single-arm trial lacks the use of a parallel control in its experimental design, a control group is typically present in the form of an external control, such as a target value or historical study control. Target value control sets a goal for the utility to be achieved in the experiment based on the best-effect value obtained from a previous study or an industry-standard treatment. A historical control study uses the results of a high-quality study as controls, where the characteristics of the historical study population and the evaluated effect indicators were consistent with those of the current study. Therefore, the selection of controls outside the single-arm trial is also a critical aspect. If not appropriately selected, the effects of confounding factors will be substantially elevated. The increased availability of electronic medical records has made historical control data readily accessible. However, the selection of appropriate controls for baseline patient characteristics and diagnostic criteria is crucial because of a high degree of bias. Propensity score matching or stratified analyses can be used to reduce confounding biases.

Principle of balance

The principle of balance is very important when designing single-arm clinical trials. Researchers need to carefully consider inclusion and exclusion criteria, which can affect the conduct of trials, the interpretation of results and the safety of patients. Strict inclusion and exclusion criteria can result in a study population that is not representative of the broader population, affecting the ability to extrapolate results and determine the effectiveness of treatments. Therefore, the internal and external validity of the study needs to be weighed when developing inclusion and exclusion criteria. In addition, balanced comparability between the two groups can be achieved by matching the control group. The effect index of matching control group should be representative, objective and referential. Representativeness means that the evaluation indicators can best represent the effect of the intervention and meet the accepted standards of the industry. Objectivity means that the indicators used (such as laboratory tests, imaging tests and key clinical events) are objective and not influenced by subjective factors. Referrability indicates that this index has been widely used as the main therapeutic effect evaluation index in similar studies. When matching the control group, care should be taken to avoid overmatching. Overmatching may result in a smaller sample size, limiting the statistical power and generalisations of the study. Therefore, it is necessary to carefully select matching indicators and matching algorithms when matching the control group to ensure balanced comparability between groups while maintaining sufficient sample size. In short, single-arm clinical trials meet the balanced comparability between groups through strict exclusion criteria and/or control matching to ensure the reliability and validity of the study. At the same time, it is necessary to weigh internal and external validity and ensure that the matching process meets the requirements of representation, objectivity and referencability.

Principle of repetition

Sample size calculation for a single-arm test is a critical aspect of the study design process. Single-arm trials require small sample sizes, making it particularly important to calculate a sufficient sample size to ensure test efficacy. Researchers must clearly define the primary endpoint of the study as a meaningful difference before and after the test. This clinical decision must be statistically significant in the design of the number of patients required in the study. For example, in a study of acute myeloid leukaemia treatment, where the primary endpoint was the overall remission rate, a review of the literature revealed that the objective response rate (ORR) of the historical study was approximately 35%, whereas the current study was projected to have an ORR of approximately 60%. 42 These rates can be used to define the study hypotheses and determine the sample size required to conduct the study. The ORR data obtained from historical studies are the target value of the effect, which is a set of widely recognised evaluation criteria obtained from a large amount of historical data. The ORR predicted by the study was the target value, which was the level expected to be achieved by the evaluation criteria for the efficacy of the intervention to be studied. The key to determining the target value was to establish a clinically meaningful superiority threshold; that is, how much higher the level of efficacy of the current study must be than the target value before it is considered clinically meaningful. Other methods of sample size estimation for survival analysis can also be used in single-arm trials. 43

Statistical analyses of the single-arm trials are mostly descriptive and exploratory. Appropriate datasets are selected for analysis to statistically describe baseline patient data. Appropriate statistical methods are selected to perform hypothesis testing on the study outcomes and controls to compare the effects of the interventions. Since relevant survival analysis indicators are included in the outcome metrics, survival curves can be plotted to visualise the prognostic progress of patients after the intervention. Several studies conduct post hoc statistical tests, such as grouping according to the efficacy and analysing and exploring the relevant factors affecting the efficacy.

Comparison with other study designs

Single-arm trials, RCTs and cohort studies are the three common research design methods with advantages and applications in different research scenarios. Figure 1 illustrates a basic diagram of these research methods and provides an initial understanding of their distinctions. Although single-arm trials are non-RCTs, they have advantages over cohort studies. However, their evidence is considered to be less scientifically robust compared with that of RCTs. Figure 2 illustrates the differences among the three research design approaches in terms of the principles of science.

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Flow chart of the three research design methods. (A) Single-arm trial; (B) randomised controlled trial; (C) conhort study.

Scientific principles embodied in the three research methods.

Medical technology is advancing rapidly and has successfully addressed many challenging diseases. However, the number of rare and difficult-to-treat diseases is increasing. Although RCTs have been considered the gold standard for demonstrating treatment efficacy, they are not always feasible or ethical to be conducted. 44 Single-arm trials are usually used when a control group cannot be found to match patients in the trial group or is unsuitable for placebo and blank controls due to ethical concerns. In these cases, single-arm trials are considered to be more easily aligned with ethical principles. The absence of a control group ensures that all patients have access to the potential benefits of the trial intervention, which is ethically advantageous. However, it must be acknowledged that all patients also face a consistent risk of harm. Unlike RCTs, single-arm trials do not require randomisation of groups, thus avoiding the ethical and implementation difficulties that may arise. In addition, sample size requirements can be reduced, saving time and resources because a single-arm trial requires only one group. They also allow for more flexibility in adjusting treatment regimens and observational metrics and better reflect real-life clinical practice. 6 Single-arm trials enable acquisition of preliminary efficacy data. Treatment response data can be collected quickly because of the requirement for only one group. This has resulted in a more rapid assessment of drug efficacy and safety. This approach can be especially valuable in emergencies or for treating rare diseases because it enables healthcare providers to offer effective treatment options to patients more quickly. Consequently, regulatory authorities may accept results from single-arm studies in certain circumstances, such as with rare diseases or specific disease subtypes with small patient populations where no effective standard treatment exists, or support expedited development using accelerated approval, conditional approval or other regulatory pathways. 45 46

Cohort and single-arm trials are commonly conducted in clinical research. However, single-arm trials are more persuasive in their evidence as non-RCTs than are cohort studies. Cohort studies can provide evidence for disease aetiology, prevention and treatment by observing and analysing the occurrence and prognosis of diseases in a population. 47 However, cohort studies may be affected by selection and measurement biases, which can cause inaccurate results. 48 49 Conversely, single-arm trials can assess the effect of an intervention by imposing this on a test group and comparing this with an external control. The study design can better control the interference of external variables and improve the accuracy and reliability of the results. Furthermore, a balanced and comparable population can be achieved in the test and control groups by selecting an external control. 6 50 Therefore, the outcomes of a single-arm trial may be more convincing and provide physicians and patients with a more reliable basis for decision-making. Although both cohort studies and single-arm trials are crucial methods in clinical research, the evidence from single-arm trials can be more persuasive and can offer more precise and reliable data for better direct clinical practice.

However, single-arm trials have certain limitations. RCTs can provide more scientific evidence. The absence of a control group means that the interpretation of results cannot rely solely on the intervention, thus reducing the reliability of the evidence. A single-arm trial does have a control but is not drawn from the same period or study as the subjects but is instead drawn from an external historical control or contemporaneous cohort study control. This introduces some bias as the subjects in the trial and external control groups could be from different populations, and therefore, less comparable. When selecting a control group, it is important to carefully screen the patients based on their baseline characteristics and diagnostic criteria. As parallel controls are lacking, comparisons could only be made with external historical data to evaluate the validity and safety of the study population. However, finding historical data that fully align with the current study design is challenging, and distinguishing the differences between studies makes it difficult to evaluate the results.

Because only one test group is present in a single-arm trial, the principles of randomisation and blinding cannot be applied, and this may introduce bias in the results. Therefore, extra care must be taken in designing and executing the trial to minimise bias and error and improve the accuracy and reliability of the results. In highly sensitive medical fields, it is essential to strive for higher levels of evidence. RCTs have always been the first choice in the design of clinical trials. Single-arm trials are only considered when it is not feasible to conduct an RCT.

In certain specific circumstances, a single-arm trial design is a feasible research design method. This is primarily because it involves only one experimental group without a control group, allowing all participants to receive treatment. However, researchers must fully acknowledge the limitations of single-arm trials in their design and implementation. These limitations may include the absence of a parallel control group, weaker interpretation of results, and the potential for selection bias in external comparison groups. To overcome these limitations and enhance the reliability and interpretability of single-arm trials, researchers must exercise caution and meticulousness when selecting external controls, determining sample sizes and setting effect measures. In conclusion, the use of single-arm trials should be carefully considered and should only be chosen when it is not possible to conduct an RCT.

Ethics statements

Patient consent for publication.

Not applicable.

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Contributors CJ and MW researched the literature and conceived the study. MW wrote the first draft of the manuscript. All authors reviewed and edited the manuscript and approved the final version of the manuscript.

Funding This work was supported by Research Center for the Development of Medicine and Health Science and Technology of the National Health Commission (No. 2023YFC3606200), the Department of Science and Technology of Zhejiang Province (No. 2023C25012) and Zhejiang Provincial Health Commission (No. 2023ZL360 and No. 2024KY1195).

Competing interests None declared.

Provenance and peer review Not commissioned; internally peer reviewed.

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