Alternating treatments design: one strategy for comparing the effects of two treatments in a single subject PMC

Table Of Content

• Illustrations and Comparison of the Results
• Procedure
• Randomization tests for restricted alternating treatments designs.
• A special latin square for the use of each subject “as his own control”
• Review of Methods to Equate Target Sets in the Adapted Alternating Treatments Design
• Data Analysis in Single-Subject Research

In both cases, the consistency of effects can be conceptualized as the degree to which variability of the effects observed in the different blocks are comparable to the average of these effects across blocks. These separate assessments are well-aligned with the recommendations for performing visual analysis (Lane et al., 2017; Ledford et al., 2019; Maggin et al., 2018). For James and Joseph, the procedure resulted in target responses that also produced low baseline levels. For Sean, after completing the target identification phase and beginning baseline, the interventionist was informed that the classroom teacher independently chose to teach some of the selected responses.

Illustrations and Comparison of the Results

From the perspective of scientific significance, one can argue that statistical analysis may be warranted as a judgment aid for determining whether there were any effects, regardless of size, because knowing this would help determine whether to continue investigating the variable (i.e., intervention). If it is decided that, under some circumstances, it is scientifically sensible to use statistical analyses (e.g., t tests, analyses of variance [ANOVAs], etc.) as judgment aids for effect detection within single case data sets, the next question is a very practical one—can we? In this context, the term safely refers to whether the outcome variables are sufficiently robust that they withstand violating the assumptions underlying the statistical test. The short answer seems to be “no,” with the qualifier “under almost all circumstances.” The key limitation and common criticism of generating statistics based on single-subject data is auto-correlation (any given data point is dependent or interacts with the data point preceding it). Because each data point is generated by the same person, the data points are not independent of one another (violating a core assumption of statistical analysis—technically, that the error terms are not independent of one another). Thus, performance represented in each data point may likely be influencing the next (Todman & Dugard, 2001).

Procedure

As such, three variations of physical prompts (i.e., partial physical(s) and full physical) were included in this assessment. For Joseph, one partial prompt and the full physical prompts were assessed whereas two variations of partial physical prompts and the full physical prompts were assessed for the other two participants. In the second condition, the interventionist provided the verbal discriminative stimulus and immediately modeled the target response (e.g., the interventionist said “Clap!” and then clapped) and waited 5 s for the participant to respond. In the third condition, the interventionist provided a gestural prompt in addition to the verbal discriminative stimulus (e.g., the interventionist said “Clap!” and then pointed to the participant’s hand) and waited 5 s for the participant to respond. The percentage of correct responding for each of these conditions was calculated by dividing the number of correct responses by the number of total responses (10) and multiplying it by 100.

Randomization tests for restricted alternating treatments designs.

This notion has a relatively long history (Edgington, 1975) and continues to be mentioned in contemporary texts (Todman & Dugard, 2001). One disadvantage of all designs that involve two or more interventions or independent variables is the potential for multiple-treatment interference. This occurs when the same participant receives two or more treatments whose effects may not be independent.

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Traditional nonparametric approaches have been advocated, but they do not necessarily avoid the autocorrelation problem and, depending on the size of the data array, there are power issues. Alternatively, if single-subject data are regarded as time-series data, there have been some novel applications of bootstrapping methodologies relying on using the data set itself along with resampling approaches to determine exact probabilities rather than probability estimates (Wilcox, 2001). In the end, effect detection is determined by data patterns in relation to the phases of the experimental design.

In addition, there is no known sampling distribution, making it impossible to derive a confidence interval (CI). CIs are important because they help create an interpretive context for the dependability of the effect by providing upper and lower bounds for the estimate. There has been a small but steady body of work addressing effect size calculation and interpretation for SSEDs. Space precludes an exhaustive review of all the metrics (for comprehensive reviews, see Parker & Hagan-Burke, 2007, and related papers from this group). There are, however, a number of points that can be made regarding the use (derivation, interpretation) of effect size indices that are common to all. The simplest and most common effect size metric is the percentage of nonoverlapping data (PND; Scruggs, Mastropieri, & Casto, 1987).

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For this study, the maintenance of the behavior after the intervention was withdrawn supports its long-term effectiveness without undermining the experimental control. The calculation is actually a mean absolute percentage error, computed when comparing different conditions, which is why this data analytical technique is abbreviated MAPEDIFF (Manolov & Tanious, 2020). Thus, the modified Brinley plot can be used to represent visually the outcome of the specific comparisons performed between measurements in an ATD with block randomization) or between phases in a multiple-baseline or an ABAB design. This follow-up intervention was conducted for a number of sessions that represented 50 % of the sessions required to reach the mastery criterion with the most successful procedure during the prompt hierarchy comparison.

Includes interpolated values, which are assumed to represent the value that would have been obtained under the condition not taking place. The comparison is only ordinal (i.e., one condition is either superior, equal or inferior to the other) without quantifying the distance. To save this article to your Google Drive account, please select one or more formats and confirm that you agree to abide by our usage policies. If this is the first time you used this feature, you will be asked to authorise Cambridge Core to connect with your Google Drive account.Find out more about saving content to Google Drive. To save this article to your Dropbox account, please select one or more formats and confirm that you agree to abide by our usage policies.

Comparing Interventions Using the Alternating Treatments Design

However, rather than having multiple baselines across participants, settings, or behaviors, the changing-criterion design uses multiple levels of the independent variable. Experimental control is demonstrated when the behavior changes repeatedly to meet the new criterion (i.e., level of the independent variable). In some cases, the simultaneous and continuous data collection in all legs of multiple-baseline designs is not feasible or necessary. Multiple-probe designs are a common variation on multiple baselines in which continuous baseline assessment is replaced by intermittent probes to document performance in each of the conditions during baseline. Probes reduce the burden of data collection because they remove the need for continuous collection in all phases simultaneously (see Horner & Baer, 1978, for a full description of multiple-probe designs). Pre-intervention probes in Condition 1 are obtained continuously until a stable pattern of performance is established.

Direct replication refers to the application of an intervention to new participants under exactly, or nearly exactly, the same conditions as those included in the original study. This type of replication allows the researcher or clinician to determine whether the findings of the initial study were specific to the participant(s) who were involved. Systematic replication involves the repetition of the investigation while systematically varying one or more aspects of the original study. This might include applying the intervention to participants with more heterogeneous characteristics, conducting the intervention in a different setting with different dependent variables, and so forth.

For example, if a treatment seemed to reduce the incidence of self-injury in a developmentally disabled child, it would be unethical to remove that treatment just to show that the incidence of self-injury increases. The second problem is that the dependent variable may not return to baseline when the treatment is removed. For example, when positive attention for studying is removed, a student might continue to study at an increased rate. This could mean that the positive attention had a lasting effect on the student’s studying, which of course would be good.

Multiple-probe designs may not be appropriate for behaviors with significant variability because the intermittent probes may not provide sufficient data to demonstrate a functional relationship. If a stable pattern of responding is not clear during the baseline phase with probes, the continuous assessment of a multiple-baseline format may be necessary. Incorporating randomization in the design boosts internal validity and scientific credibility in any type of design, including SCEDs (Edgington, 1975; Kratochwill & Levin, 2010).

If we don’t believe in unlikely events then our conclusion is tentatively that the intervention is effective, but a statistically significant result does not show the actual probability that the intervention is superior to another treatment or baseline. The alternating treatments design which is increasingly being used in single subject research is described. This design allows the differential effectiveness of two or more treatments to be investigated by presenting each of them separately in closely spaced sessions, with the order of presentation alternated. Consideration is given to the types of behavior and contexts that are most appropriate for use with this design and also to factors important for ensuring its effectiveness and the valid interpretation of the resulting data. This study replicated Seaver and Bourret (2014)’s approach to identifying effective prompt topographies prior to comparing prompt hierarchies and extended the work by providing additional support with younger populations and an alternative procedure for conducting the prompt topography assessment. The dependent variable was the percentage of correct independent responses to one-step directions.

As we have seen throughout the book, group research involves combining data across participants. Group data are described using statistics such as means, standard deviations, Pearson’s r, and so on to detect general patterns. Finally, inferential statistics are used to help decide whether the result for the sample is likely to generalize to the population. Single-subject research, by contrast, relies heavily on a very different approach called visual inspection. This means plotting individual participants’ data as shown throughout this chapter, looking carefully at those data, and making judgments about whether and to what extent the independent variable had an effect on the dependent variable. There are two potential problems with the reversal design—both of which have to do with the removal of the treatment.

Thus, consistent with all of the points made above, sound methodology (design, measurement) is the biggest determinant of valid decision making. Overall, the four issues discussed above—effect detection, magnitude of effect, quality of the inference, and practice decisions—reflect the critical dimensions involved in the analysis of SSED. The importance of any one dimension over the other will likely depend on the purpose of the study and the state of the scientific knowledge about the problem being addressed. Finally, related to several different comments in the preceding sections regarding practical significance, there is the issue of interpreting effects directly in relation to practice in terms of eventual empirically based decision making for a given client or participant. At issue here is not determining whether there was an effect and its standardized size but whether there is change in behavior or performance over time—and the rate of that change.

Moreover, the use of randomization makes possible and valid the use of randomization tests, a kind of statistical test that makes no distributional assumptions and no assumptions about random sampling (Edgington & Onghena, 2007; Levin et al., 2019). The evidence provided by the application of a randomization test to an individual’s data is more closely related to the typical aims in behavioral sciences (Craig & Fisher, 2019). Applied researchers need to be cautious only when performing multiple statistical tests, in relation to potentially committing a Type I error. Finally, statistical inference can be expressed as a confidence interval constructed around an effect size estimate, thanks to inverting the randomization (Michiels et al., 2017). A different comparison can be performed, comparing data paths, rather than only actually obtained measurements, using ALIV (Manolov & Onghena, 2018) and the visual structured criterion (Lanovaz et al., 2019).