Chapter 12: Single-Subject Designs

The demands of traditional experimental methods are often seen as barriers to clinical inquiry for several reasons. Because of their rigorous structure, experiments require control groups and large numbers of homogenous subjects, often unavailable in clinical settings. In addition, group studies typically take measurements at only two or three points in time, potentially missing variations in response that occur over time. Finally, the experimental model deals with group averages and generalizations across individuals, which may not allow the researcher to differentiate characteristics of those patients who responded favorably to treatment from those who did not improve. Therefore, although generalizations are important for explaining behavioral phenomena, clinicians understand that group performance is relevant only if it can be used to understand and predict individual performance.

To illustrate this dilemma, consider a study that was done to determine if the occurrence of stuttering would be different if adults read aloud at "usual" or "fast as possible" rates.¹ A group of 20 adults was tested, and no significant difference was seen between the two conditions based on a comparison of group means. However, a closer look at individual results showed that 8 subjects actually decreased their frequency of stuttering, one didn't change, and 11 demonstrated an increase during the faster speaking condition. The group analysis obscured these individual variations.² These results could mean that there is no consistent effect, but they may also point to specific subject characteristics that account for the differences.

Single-subject designs^∗ provide an alternative approach that allows us to draw conclusions about the effects of treatment based on the responses of a single patient under controlled conditions. Through a variety of strategies and structures, these designs provide a clinically viable, controlled experimental approach to the study of a single case or several subjects, and the flexibility to observe change under ongoing treatment conditions. Given the focus of evidence-based practice on clinical decision making for individual patients, these designs are especially useful.

Single-subject designs require the same attention to logical design and control as other experimental designs, based on a research hypothesis that indicates the expected relationship between an independent and dependent variable and specific operational definitions that address reliability and validity. The independent variable is the intervention. The dependent variable is the patient response, defined as a target behavior that is observable, quantifiable, and a valid indicator of treatment effectiveness.

Single-subject designs can be used to study comparisons between several treatments, between components of treatments, or between treatment and no-treatment conditions. The purpose of this chapter is to describe a variety of single-subject designs and to explore issues associated with their structure, application and interpretation.

Single-subject designs are structured around two core elements that distinguish them from a case study or group studies: repeated measurement and design phases.

Repeated Measurement

Single-subject designs involve the systematic collection of repeated measurements of a behavioral response over time, usually at frequent and regular intervals, such as at each treatment session (which may be more than once a day), each day or once a week. These repeated assessments are required to observe trends and patterns in the data and to evaluate variability of the behavioral response over time. This type of variability is obscured in group studies when behavior is measured only before and after treatment. The advantage of repeated assessment is that the researcher can observe response patterns and modify the design as the study progresses to obtain the most meaningful outcome.

Design Phases

The second core element of a single-subject design is the delineation of at least two testing periods, or phases: a baseline phase, prior to treatment, and an intervention phase. The target behavior is measured repeatedly across both baseline and intervention phases. The baseline phase provides information about responses during a period of "no treatment," or a control condition. This initial observation period reflects the natural state of the target behavior over time in the absence of the independent variable. The assumption is that baseline data reflect the ongoing effects of background variables, such as daily activities, other treatments and personal characteristics on the target behavior. When treatment is initiated, changes from baseline to the intervention phase should be attributable to intervention. Therefore, baseline data provide a standard of comparison for evaluating the potential cause-and-effect relationship between the intervention and target behavior.

Design phases are traditionally plotted on a line graph, as shown in Figure 12.1, with magnitude of the target behavior along the Y-axis and time (sessions, trials, days, weeks) along the X-axis. Using conventional notation, the baseline period is represented by the letter A and the intervention period by the letter B. To facilitate description, this design, with one baseline phase and one intervention phase, is called an A-B design.

The collection of baseline data is the single feature of a single-subject design that particularly distinguishes it from clinical practice, case studies and traditional experimental designs, where treatment is initiated immediately following assessment. From a research standpoint, the traditional approach makes it impossible to determine which components of treatment actually caused observed changes, or more important, if observed changes would have occurred without intervention. Just as we need a control group to validate group comparisons, we must have a control period to make these determinations for a single-subject experiment.

Ethical objections often arise when the baseline concept is introduced, just as they do when a control group is proposed for a group comparison study. Two points must be made in this regard. First, we can argue that it is not unethical to withhold treatment for a relatively short period when we are unsure about the effectiveness of the intervention in the first place. Indeed, it may actually be unethical to continue to provide an inferior or ineffective treatment without testing it experimentally. It is, however, important to realize that this approach is not appropriate for studying every type of intervention, such as treatments for critical or life-threatening situations, where treatment effects are not questioned and withholding treatment would be harmful. Second, collecting baseline data does not mean that the clinician is denying all treatment to the patient. It only means that one portion of the patient's total treatment is being isolated for study while all other treatments and activities are continued as background.

Baseline Characteristics

Two characteristics of baseline data are important for interpretation of clinical outcomes: stability, which reflects the consistency of response over time, and trend, or slope, which shows the rate of change in the behavior. The most desirable baseline pattern demonstrates a constant level of behavior with minimal variability, indicating that the target behavior is not changing (see Figure 12.2A). Therefore, changes that are observed after the intervention is introduced can be confidently attributed to a treatment effect. If treatment has no effect, we would expect to see this baseline pattern continue into the intervention phase.

A variable baseline (Figure 12.2B) can present a problem for interpretation. When this type of pattern emerges, it is generally advisable to continue to collect baseline data until some stability is achieved. With extreme variability, the researcher is obliged to consider what factors might be influencing the target behavior to create such an erratic response. Sometimes cyclical patterns are evident, perhaps with variations corresponding to days of the week, time of day, or regular events occurring in the subject's life. If these factors continue to operate during intervention, they could easily obscure treatment effects.

An accelerating baseline (Figure 12.2C) or a decelerating baseline (Figure 12.2D) indicates that a change in the target behavior is occurring without intervention. Either type of trend may represent improvement or deterioration, depending on the target behavior. Trends can also be characterized as stable or unstable; that is, the rate of change may be constant (as in Figure 12.2C) or variable (as in Figure 12.2D). Trends in baseline data must be identified to determine if responses that are observed following treatment represent true change.

Length of Phases

One of the first questions clinicians ask when planning single-subject experiments concerns how long phases should be. Single-subject designs provide some flexibility in these choices, allowing for consideration of the type of patient, the type of treatment, and the expected rate of change in the target behavior. This flexibility differentiates the single-subject design from traditional designs where onset and duration of treatment are established and fixed prior to experimentation, regardless of how the patient responds. There are some guidelines that can be followed to assist in these decisions.

It is generally desirable to use relatively equal phase length. It is not uncommon, for example, to find that researchers preset intervals of 1 week for each phase in a design when daily measurements are taken. This practice helps to control for potential time-related factors such as maturation or the motivational influence of continued attention over prolonged treatment periods. Despite these plans, however, it is usually advisable to extend baseline or intervention phases until stability is achieved, or at least until one is sure that responses are representative of the true condition under study. Most important, it is essential that the length of time within each phase is sufficient to capture any changes that will occur over time.

Because trend is an important characteristic of repeated measurements, there must be a minimum of three to four data points in each phase. The application of some analysis procedures is enhanced by having 12 or more points within each phase to establish stability.⁷ Clearly, the greater the number of data points, the more obvious trends will become. It is useful to remember that the intervals used for repeated measurements need not represent single days. When patient behaviors change rapidly in response to intervention, more than one session can be plotted within a day, so that a sufficient number of data points can be obtained in a short period.

Target behaviors can reflect different response systems and may focus on impairments, activity limitations or measures of disability. Measurements may deal with overt motor behaviors, such as functional performance, range of motion (ROM), strength or gait characteristics. We can also assess physiological reactions, such as blood pressure or exercise responses, and verbal reactions, such as the number of correct responses to specific questions or subjective feelings of pain. Assessment techniques vary, depending on the types of variables designated as target behaviors. One benefit of the singlesubject approach is the ability to develop individualized measurement systems that reflect a patient's performance in a clinically relevant way. For instance, specific functional tasks may be emphasized that indicate a patient's major limitations. The choice of a target behavior can be an important first step in making a single-subject study meaningful.

Measuring the Target Behavior

Although many clinical variables are typically assessed using qualitative values, they must be quantified in some way to be used as experimental data. One of the major advantages of the single-subject approach is that it provides a mechanism for quantifying even the most subjective clinical behaviors. The most common techniques for measuring behaviors within single-subject designs are frequency, duration and magnitude measures.

A frequency count indicates the number of occurrences of the behavior within a fixed time interval or number of trials. For example, we can count the number of times a particular gait deviation occurs, the number of times a patient can correctly name objects, or the number of times a patient loses her balance during a defined treatment session. Operational definitions for frequency counts must specify how the target behavior is distinguished from other responses and exactly what constitutes an occurrence and nonoccurrence of the behavior. For instance, if a patient attempts an exercise and achieves only partial range, is that counted as an occurrence? If a patient begins to fall over but catches herself by reaching for the wall, is that considered loss of balance?

Frequency can be expressed as a percentage, by dividing the number of occurrences of the target behavior by the total number of opportunities for the behavior to occur. This method is often used in studies where accuracy of performance (percentage correct) is of primary interest. Frequency counts can also be translated into rates. Rate refers to the number of times a behavior occurs within a specified time period. It is calculated by dividing the total number of occurrences of the behavior by the total time (seconds, minutes or hours) during which the behavior was observed. For example, we can measure ambulation in steps per minute or endurance in repetitions per minute.

A useful procedure for measuring repetitive behavior is called interval recording, which involves breaking down the full measurement period into preset time intervals, and determining if the behavior occurs or does not occur during each interval. For instance, Dave⁸ studied the effects of vestibular stimulation on stereotypic body-rocking behaviors in three adults with profound mental retardation. He monitored the behavior for a total of 5 minutes, looking at the occurrence or nonoccurrence of rocking within consecutive 15-second intervals.

Target behaviors can also be evaluated according to how long they last. Duration can be measured either as the cumulative total duration of a behavior during a treatment session or as the duration of each individual occurrence of the behavior. Operational definitions for duration measures must specify criteria for determining when the behavior starts and when it ends. For example, we can measure how long a patient stays in a balanced standing posture within a single trial or over a treatment session, or we can time how long it takes for a patient to complete a specific functional task, such as buttoning a shirt.

Many clinical variables are measured using some form of instrumentation that provides a quantitative score, which may be a summary score, a subscale score or a single test value. For example, Shumway-Cook and co-workers⁹ used a forceplate to assess the effect of balance training on movement of the center of pressure and time to stabilization in six children with cerebral palsy. Bastille and Gill-Body¹⁰ used scores on the Berg Balance Scale and the Stroke Impact Scale as an indicators of the effectiveness of yoga-based exercise program for patients with chronic poststroke hemiparesis. These examples illustrate the potential for using single-subject designs to study changes in outcomes, including impairments, activity limitations and disability measures.

Choosing a Target Behavior

Because patients usually present several clinical problems, choosing one specific problem as the focus of an experiment can be difficult. To focus on one target behavior, it is often necessary to define complex behaviors and determine which component of the behavior is most problematic. It is useful to consider the relative stability with which a behavior is expected to respond. It is also important to establish that a specific intervention is readily available to address the target behavior, that the behavior is a valid indicator of that intervention's effectiveness, and that the treatment will cause an observable change in the behavior. Finally, choice of a target behavior may be influenced by available instrumentation and clinical goals. Researchers can also look at several target behaviors simultaneously, to examine their potential interaction or to document the relationship between impairments and functional measures.

In addition, a measurement method must be chosen that will reflect the element of performance that is of primary concern. Is it how often a patient can perform a particular task, or how long a behavior can be maintained? Is the number of correct responses or incorrect responses of interest? Or is it simply whether or not the behavior occurred? Each measurement method will provide a different perspective of the target behavior, which will obviously influence how the data will be interpreted.

Reliability is important in single-subject research as it is in any form of clinical inquiry. Because the single-subject experiment focuses on observation of behaviors in a clinical setting, reliability is usually assessed concurrently with data collection, rather than in a separate pilot study. Researchers usually report interrater reliability using a measure of percentage agreement between observers (see Chapter 26). Reliability checks are performed by having two testers simultaneously observe the target behavior at several sessions across each phase of the study. An agreement score is obtained for each session, and results are then reported as a range of agreement scores or as an average.^†

The element that most clearly characterizes an experimental research design is its ability to control for threats to internal validity (see Chapter 9). Unfortunately, the basic A-B single-subject design is limited in this respect. Consider the following example:

Figure 12.3 shows the development of language comprehension for one child in this study. Stable responses were observed over a 9-week baseline phase. Immediately following the onset of occupational therapy, scores rise markedly, suggesting at first glance that the therapy was instrumental in achieving this change. But is this conclusion definitive? Did other events or changes within the subject occur coincidentally at the same time treatment was initiated that could have accounted for the observed change? In other words, is this conclusion internally valid?

Note that several other events may be associated with this change. Speech therapy was begun 1 week later (D), an aphasia class started at 16 weeks (E), and a developmental therapy program began at 25 weeks (F). With this design, it is impossible to conclude that the occupational therapy treatment was the causative factor in improving language comprehension scores.

To strengthen the control in this design, we must include some other form of evidence that the treatment was indeed responsible for observed changes, evidence that will discredit alternative hypotheses for explaining treatment outcomes. Within a single-subject strategy, this additional control is provided by replication of effects, which can be accomplished in several ways. Phases can be repeated by withdrawing and reinstating baseline and treatment conditions or by alternating two or more interventions. We can also replicate effects across more than one subject or within one subject across multiple conditions or behaviors. The more often an effect can be replicated within a design, the stronger the design controls against potential threats to internal validity. These strategies form the basis for structuring single-subject designs.

Experimental control within a single-subject design can be achieved through withdrawal of intervention, to demonstrate that the target behavior occurs only in the presence of treatment. The withdrawal design includes a second baseline period, but may also include a second intervention period.

A-B-A Design

The A-B-A design replicates one baseline phase following intervention. The premise of this design lies in its ability to show that behavioral changes are evident only in the presence of the intervention, during Phase B. If changes in the target behavior are not maintained during the second baseline period, one can logically conclude that the treatment was the factor causing the changes observed during the intervention phase. Internal validity is controlled because it is highly unlikely that confounding factors would coincidentally occur at both the onset and the cessation of treatment. If other variables were responsible for changes seen in the target behavior during the first two phases, the behavior would not be expected to revert to baseline levels during the withdrawal phase.

The results for this study are shown in Figure 12.4. The subject's scores showed an initial improvement during baseline, but then leveled off. Clear improvement was seen during the intervention phase. The increase in gait speed was somewhat variable, but maintained an increasing trend. A decrement in performance was seen when the intervention was removed, but improvement was seen again over time. The replication of effects over a second baseline period provide support for the intervention.

The obvious problem with the A-B-A design is that the behavior must be reversible. This is often not the case. Any response that is learned or that creates permanent change will not show a decrement when treatment is withdrawn. Consider the following example:

As shown in Figure 12.5, pain was relatively stable during the first baseline, showed a linear decline during intervention, and continued to decline during the second baseline phase. Pain level was clearly decreased starting at the point of intervention, but because of the effectiveness of the treatment, continued to decrease during the second baseline phase.

A-B-A-B Design

Experimental control and clinical relevance can be strengthened through the use of an A-B-A-B design, which provides initial baseline data and ends on an intervention phase. The major advantage of this design is that it provides two opportunities to evaluate the effects of the intervention. If effects can be replicated during two separate intervention phases, controlling for internal validity, the evidence is quite strong that behavioral change was directly related to the treatment.

Figure 12.6 shows results for one subject for this study. Weight distribution was plotted as a ratio of the percent weight on the affected limb over total body weight; therefore, the goal was to achieve higher ratios. Although performance is variable, there is clearly a declining ratio during both baseline phases, and an increasing ratio during both intervention phases.

The A-B-A-B design faces the same limitations as the A-B-A design, in that behaviors must be reversible to see treatment effects. If, however, the target behavior does not revert to original baseline values, but stays level during the second baseline, the A-B-A-B strategy still makes it possible to demonstrate change if there is further improvement during the second intervention phase.

The use of withdrawal is limited in situations where ethical considerations of withdrawal prevail and where behaviors are either nonreversible or prone to carryover effects. When practical replication cannot be achieved, a multiple baseline design can be used, where effects are replicated across subjects, across treatment conditions, or across multiple target behaviors. The multiple-baseline approach allows for use of the basic A-B format as well as withdrawal variations.

The multiple baseline design demonstrates experimental control by first requiring the concurrent collection of baseline data across a minimum of three data series. When all baselines exhibit sufficient stability, the intervention is applied only to the first series, while the other baselines are continued. When the first series achieves stability during treatment, intervention is introduced into the second series. Stability can be achieved either as a constant trend (acceleration or deceleration) or as a level response. This process is repeated on a staggered basis for all remaining baselines. By allowing each baseline to run for a different number of data points, systematic changes in the target behavior that are correlated with the onset of intervention can be reliably attributed to a treatment effect. Experimental control is strengthened by demonstrating that baselines are independent; that is, change is observed only when intervention is applied and does not occur during baseline periods. Some examples will help to illustrate this process.

Sometimes it is of interest to study the effect of one intervention on several related clinical behaviors. In the multiple baseline design across behaviors, the researcher monitors a minimum of three similar yet functionally independent behaviors in the same subject that can be addressed using the same intervention. Each target behavior is measured concurrently and continuously, until a stable baseline is achieved. The intervention is then introduced sequentially across the different behaviors.

The results shown in Figure 12.7 demonstrate treatment effects most clearly for commenting behavior, with moderate gains in vocal imitation and dramatically variable changes in requests. Obviously, the multiple baseline design across behaviors requires that the targeted behaviors are similar enough that they will all respond to one treatment approach, and that they are functionally independent of one another so that baselines will remain stable until treatment is introduced. With many social and physical variables, this assumption can be problematic.

If we had used the A-B format for only one of these strategies, these results would not have been so definitive because of potential threats to internal validity; however, because the results have been replicated across three conditions at staggered times, it is highly unlikely that external factors could have coincidentally occurred at the time each treatment was initiated to cause the response change. One of the major advantages of the multiple-baseline approach is that replication and experimental control can be achieved without withdrawal of treatment.

In a multiple baseline design across subjects, one intervention is applied to the same target behavior across three or more individuals who share common relevant characteristics.

In this study, all subjects showed at least a consistent level of response, with no decrement in GMFM scores. The authors concluded that the intermittent intensive therapy schedule was well tolerated and effective compared to the standard schedule of 2 treatments/week.

In the multiple baseline design across conditions, one behavior is monitored on one individual, with the same treatment applied sequentially across two more environmental conditions. These may be different treatment settings, different instructional arrangements, or different clinicians. Experimental control in this design can be demonstrated only if the target behavior is independent of the environment. Therefore, behavioral change in one environment will not influence behavior in other settings.

In this study, the researchers saw that the frequency of relevant sentences clearly increased with the use of the software program during play. The level of response was minimal during hygiene activities, and the authors commented that this was not an activity the children enjoyed.

Nonconcurrent Multiple Baseline Design

A basic premise of the multiple baseline design across subjects is that baseline data are available for all subjects simultaneously so that temporal effects cannot contaminate results. A variation of this design, called a nonconcurrent multiple baseline design, can be used in the common clinical situation in which similar subjects are not available for concurrent monitoring.¹⁸ This approach requires that the researcher arbitrarily determines the length of several baselines, such as 5, 10 and 15 days. When a subject who matches the study criteria becomes available, he is randomly assigned to one of the predetermined baseline lengths. Baseline data are collected, and treatment is introduced at the appropriate time, assuming baselines are sufficiently stable. If baseline data are too variable, the subject is dropped from the study. As other subjects become available, they are randomly assigned to the remaining baselines.

The results for three patients are shown in Figure 12.8. We can see that the responses in these subjects are quite variable, making it more difficult to understand the effect of intervention. The trend lines in each intervention phase, however, do suggest that higher scores (decreased neglect) were evident for each subject. We will discuss interpretation of these trend lines shortly.

The benefit of the nonconcurrent baseline approach is obvious in terms of practical research requirements; however, it is a weaker design than the standard multiple baseline approach because external factors related to the passage of time may be different for each baseline. For instance, patients may be tested during different seasons of the year, or the clinical environment may change over time. Therefore, the nonconcurrent multiple baseline design should be used only when a sufficient number of subjects are not available for concurrent study. Because of this potential weakness as an experimental design, the number of subject replications should be increased as an additional element of control.

Withdrawal designs represent treatment-no treatment comparisons. Single-subject designs can also be used to compare the effects of two treatments.

Alternating Treatment Design

One strategy for studying multiple treatments involves the alternating treatment design. The essential feature of this design is the rapid alternation of two or more interventions or treatment conditions, each associated with a distinct stimulus. Treatment can be alternated within a treatment session, session by session, or day by day. This design can be used to compare treatment with a control or placebo or to compare two different interventions, to determine which one will be more effective. Data for each treatment condition are plotted on the same graph, allowing for comparison of data points and trends between conditions.

Scheduling of alternated treatments will depend on the time needed to complete the treatment condition at each session and the potential for carryover from trial to trial. Because treatment conditions are continuously alternated, sequence effects are of primary concern. This concern must be addressed either by random ordering of the treatment applications on each occasion or by systematic counterbalancing. In addition, other conditions that might affect the target behavior, such as the clinician, time of day, or setting should be counterbalanced.

Figure 12.9 illustrates the outcome for this study. With relatively stable baselines staggered from 4 to 10 sessions, we can see clear changes at the initiation of the interventions. The advantage of using the alternating treatment design over an A-B-A-B design for this type of question is that a prolonged withdrawal is unnecessary, and results can be obtained more quickly.

The alternating treatment design is also called a between-series strategy, indicating that analysis is not specifically concerned with trends over time, but that the primary focus is comparison of data points between treatment conditions at each session. For instance, in Figure 12.9 we see that the visual feedback condition was generally lower than the combined condition on each day. This design will work even under conditions where responses are very variable or where treatment conditions exhibit similar trends.

It is actually unnecessary to include a baseline phase in an alternating treatment design, just as a control group may not be included in group designs in which two treatments are compared. Baseline data can, however, be useful in situations where both treatments turn out to be equally effective, to show that they are better than no treatment at all.

Because target behaviors are measured in rapid succession, the alternating treatment design is appropriate where treatment effects are immediate and where behavior is a clear consequence of one specific treatment. The target behavior must be capable of changing quickly, and the interventions must be able to trigger those changes as they are applied and withdrawn. The alternating treatment design is not useful in situations where behavior takes time to change, where learning effects or physiological changes are cumulative and long term or where multiple-treatment interference is likely. In those situations, it would be difficult to separate out the effects of each intervention in alternated trials. The major advantage of the alternating treatment design is that it will usually provide answers to questions of treatment comparison in a shorter time frame than designs that require introduction and withdrawal of multiple treatment phases over time.

Multiple Treatment Designs

Using a variation of the withdrawal design, a multiple treatment design typically involves the application of one treatment (B) following baseline, the withdrawal of that treatment, and introduction of another treatment (C). These two interventions can represent two different treatments or one intervention and a placebo. In an A-B-C-A design, assuming the two treatments have independent and differential effects, we should be able to see differences in the target responses across the four phases of the study. By replicating the A phase, we provide the control needed to document differences between the two treatments.

Figure 12.10 shows the results for the first subject's double support time. Results show great variability, with some increase during the period of weight at the waist. This was considered a deterioration in the response. It is important to note in multiple treatment designs, that only adjacent phases can be compared. Therefore, the C phase cannot be compared to the initial baseline, but only to the reversal in the final phase.

Single-subject designs can also be used to examine the interactive or joint effect of two or more treatments as they are applied individually or as a treatment package. Interactive designs are based on variations of an A−B−BC strategy (sometimes written A−B−B+C), where BC represents the combined application of interventions B and C. In this design, Treatment C is superimposed on Treatment B, so that combined and separate effects can be observed. When structuring this type of design, treatment effects should be replicated at least once to achieve internal validity. The study of interactions requires that only one variable be changed at a time from phase to phase, such as BC−B or B−BC, so that changes from isolated to combined conditions can be assessed across adjacent phases.

Data analysis in single-subject research is based on evaluation of measurements within and across design phases, to determine if behaviors are changing and if observed changes during intervention are associated with the onset of treatment. Visual analysis of the graphic display of data is the most commonly used method. Many researchers prefer to use a form of statistical analysis to corroborate visual analysis of time-series data, to determine whether differences between phases are meaningful, or if they could have occurred by chance alone. Several authors have described methods for analyzing these designs.^3,22,23,24 Statistical analysis provides a more quantitative approach to determine whether observed changes are real or chance occurrences. In this section we examine both approaches and discuss some of the more commonly used methods for analyzing data from single-subject experiments.

Visual Analysis

Visual analysis is used most often to analyze single-subject data because it is intuitively meaningful. In contrast to statistical analysis in group designs, this approach focuses on the clinical significance of outcomes.²⁵ Data collected in a single-subject experiment can be analyzed in terms of within-phase and between-phase characteristics. Data within a phase are described according to stability, or variability, and trend, or direction of change. An analysis of changes between phases is used to evaluate the research hypothesis. Phase comparisons can be made only across adjacent phases. These comparisons are based on changes in three characteristics of the data: level, trend and slope. Figure 12.11 shows several common data patterns that reflect different combinations of these characteristics.

Level

Changes in level refer to the value of the dependent variable, or magnitude of performance, at the point of intervention. It is judged by comparing the value of the target behavior at the last data point of one phase with its value at the first data point of the next adjacent phase. For example, Figures 12.11 A and B show a change in level from the baseline to the intervention phase.

Level can also be described in terms of the mean or average value of the target behavior within a phase. This value is computed by taking the sum of all data points within a phase and dividing by the number of points. Mean levels can be compared across phases, as a method of summarizing change. For instance, in Figure 12.11A, mean levels for each condition are shown by dotted lines. Means are useful for describing stable data that have no slope, as stable values will tend to cluster around the mean; however, when data are very variable or when they exhibit a sharp slope, means can be misleading. For example, in Figure 12.11C, the dotted lines represent the mean score within each phase. On the basis of these values, one might assume that performance did not change once intervention was introduced. Obviously, this is not the case. Mean values should always be shown on a graph of the raw data to reduce the chance of misinterpretation.

Trend

Trend refers to the direction of change within a phase. Trends can be described as accelerating or decelerating and may be characterized as stable (constant rate of change) or variable. Trends can be linear or curvilinear. Changes in linear trend across phases are displayed in Figures 12.11A and C. In Figure 12.11D, no trend is observed during baseline, and a curvilinear trend is seen in the intervention phase; that is, the data change direction within the intervention phase.

A trend in baseline data does not present a serious problem when it reflects changes in a direction opposite to that expected during intervention. One would then anticipate a distinct change in direction once treatment is initiated; however, it is a problem when the baseline trend follows the direction of change expected during treatment. If the improving trend is continued into the intervention phase, it would be difficult to assess treatment effects, as the target behavior is already improving without treatment. It is important to consider what other factors may be contributing to this improvement. Perhaps changes reflect maturation, a placebo effect or the effect of other treatments. Instituting treatment under these conditions would make it difficult to draw definitive conclusions. When trends occur in the baseline, it is usually advisable to extend the baseline phase, in hopes of achieving a plateau or reversal in the trend, and to try to identify causative factors. Those factors may be useful interventions in their own right and may provide the basis for further study.

The slope of a trend refers to its angle, or the rate of change within the data. Slope can only be determined for linear trends. In Figure 12.11B, trends in both phases have approximately the same slope (although their level has changed). In Figure 12.11E, both phases exhibit a decelerating trend; however, the slope within the intervention phase is much steeper than that in the baseline phase. This suggests that the rate of change in the target behavior increased once treatment was initiated.

Data analysis in single-subject research has traditionally focused on visual interpretation of these characteristics. Unfortunately, real data can be sufficiently variable that such subjective determinations are often tenuous and unreliable. For instance, look back at the data in Figure 12.8 for measures of unilateral neglect. Although it is relatively easy to determine that the level of response changed between the baseline and the treatment phase, it would not be so easy to determine the trend or slope in these data based solely on visual judgment.

Although interrater reliability of visual analysis is not necessarily strong,^22,26,27 the reliability of assessing trend is greatly enhanced by drawing a straight line that characterizes rate of change.^28,29,30,31 Several procedures can be used. Lines drawn freehand are generally considered unacceptable for research purposes. The most popular method involves drawing a line that represents the linear trend and slope for a data series. This procedure results in a celeration line, which describes trends as accelerating or decelerating. Linear regression procedures can be used to draw a line of best fit, although this technique is used less often (see Chapter 24).

Celeration Line

A celeration line is used to estimate the trend within a data series. We will demonstrate the steps in drawing a celeration line using the hypothetical data shown in Figure 12.12A. Although we will go through the process for the baseline phase only, in practice a separate celeration line can be computed for each phase in the design. Celeration lines are illustrated in Figures 12.4, 12.6 and 12.8.

The first step is to count the number of data points in the phase and then to divide those points into two equal halves along the X-axis. A vertical line is drawn to separate the two halves, as shown by the dotted line in Figure 12.12B. In this example, there are 10 data points in the baseline phase. Therefore, 5 points fall in each half of the phase. If an odd number of data points were plotted, the line would be drawn directly through the middle point. The second step is to divide these halves in half again, as shown by the broken vertical lines in Figure 12.12C. With 5 data points, the line is drawn through the third point in each half. If there were an even number of data points in each half, the line would be drawn directly between the two middle points.

The next step is to determine the median score for each half of the phase (using the halves created by the dotted vertical line). The median score divides the data in half along the Y-axis. This point is obtained by counting from the bottom up toward the top data point within each half phase. The point that divides the series in half vertically is the median score. For instance, in Figure 12.12B, there are 5 data points in the first half of the phase. Therefore, the third score will divide the series in half vertically. If there were an even number of points, the median would be midway between the two middle points. For our example, counting from the bottom up, these scores are 3, 3, 4, 5 and 5. The median score is 4. For the second half of the phase, scores are 5, 6, 6, 6, and 7, with a median of 6. A horizontal line is then drawn through each median point until it intersects the broken line, as shown in Figure 12.12C. Finally, a straight line is drawn connecting the two points of intersection. This is the celeration line, shown in Figure 12.12D.

Calculating Slope

The slope of the celeration line can be calculated to estimate the rate of change in the target behavior. Slope is computed by taking Y values on two points along the celeration line, usually spaced 1 week apart (although any useful time period can be used). The numerically larger value is divided by the smaller value to determine the slope. For example, in Figure 12.12E, the line is at 4 on Day 3 and at 6 on Day 9. Therefore, the slope of the line is 6/4 = 1.50. By looking at the direction of the trend line, we can determine that this target behavior is increasing at an average rate of 1.50 times per week. Slopes can be calculated for each phase in the design, and compared to determine if the rate of change in the target behavior is accelerating or decelerating. The difference between slopes of adjacent phases can be used to provide a numerical estimate of how intervention changes the rate of response.

Split Middle Line

The celeration line demonstrates trend in the data. The line can also be used to represent a measure of central tendency using the split-middle technique. The split middle line divides the data within a phase into two equal parts; therefore it represents a median point within the phase. To determine if the celeration line fits this model, the final step is to count the number of points on or above and on or below the line, and then to adjust the celeration line up or down if necessary so that the data are equally divided. The adjusted line must stay parallel to the original line; that is, the slope of the line does not change. In many cases, the line will not have to be adjusted. In Figure 12.12, for example, there are four points below the celeration line, four points above it and two points directly on the line. Therefore, we do not have to make any adjustments.

The split-middle line can be used to compare the trend of data across two adjacent phases.^‡ To illustrate this method, we have taken the split-middle line that was drawn for baseline data in Figure 12.12, and recreated it in Figure 12.13. The line has been extended from the baseline phase into the intervention phase. If there is no difference between the phases, then the split-middle line for baseline data should also be the split-middle line for the intervention phase. Therefore, 50% of the data in the intervention phase should fall on or above that line, and 50% should fall on or below it. If there is a difference, and treatment has caused a real change in observed behavior, then the extended baseline trend should not fit this pattern.

Statistically, we propose a null hypothesis (H₀) which states that there is no difference across phases; that is, any changes observed from baseline to the intervention phase are due to chance, not treatment. We also propose an alternative to H₀, which can be phrased as a nondirectional or directional hypothesis; that is, we can state that we expect a difference between phases (nondirectional) or that responses will increase (or decrease) from baseline (directional). For the example shown in Figure 12.13, let's assume we propose that there will be an increase in response with intervention.

To test H₀, we apply a procedure called the binomial test, which is used when outcomes of a test are dichotomous; in this case data points are either above or below the split middle line. To do the test, we count the number of points in the intervention phase that fall above and below the extended line (ignoring points that fall directly on the line). In our example, one point falls below the line and nine points fall above the line. Clearly, this is not a 50–50 split. On the basis of these data, we would like to conclude that the treatment did effect a change in response; however, we must first pose a statistical question: Could this pattern, with one point below and nine points above the line, have occurred by chance? Or can we be confident that this pattern shows a true treatment effect?

We answer this question by referring to Appendix Table A.11, which lists probabilities associated with the binomial test. Two values are needed to use this table. First, we find the appropriate value of n (down the side), which is the total number of points in the intervention phase that fall above and below the line (not counting points on the line). In this case, there is a total of 10 points. We then determine if there are fewer points above or below the extended line. In our example, there are fewer points (one) below the line. The number of fewer points is given the value x; therefore, x = 1. The probability associated with n = 10 and x = 1 is .011, that is, p = .011.

The probabilities listed in Table A.11 are one-tailed probabilities, which means they are used to evaluate directional alternative hypotheses, as we have proposed in this example. If a nondirectional hypothesis is proposed, a two-tailed test is performed, which requires doubling the probabilities listed in the table.

The probability value obtained from the table is interpreted in terms of a conventional upper limit of p = .05. Probabilities that exceed this value are considered not significant; that is, the observed pattern could have occurred by chance. In this example, the probability associated with the test is less than .05 and, therefore, is considered significant. The pattern of response in the intervention phase is significantly different from baseline. The concept of probability testing and statistical significance is covered in detail in Chapter 18.

Two Standard Deviation Band Method

Another useful method of analysis is the two standard deviation band method. This process involves assessing variability within the baseline phase by calculating the mean and standard deviation of data points within that phase (see Chapter 17 for calculation methods for these statistics). Use of the two standard deviation band method is shown in Figures 12.5 and 12.10.

To illustrate this procedure, we have again used the hypothetical data reproduced in Figure 12.14. The solid line represents the mean level of performance for the baseline phase, and the shaded areas above and below this line represent two standard deviations above and below the mean. As shown in the figure, these lines are extended into the intervention phase. If at least two consecutive data points in the intervention phase fall outside the two standard deviation band, changes from baseline to intervention are considered significant. In this example, the mean response for baseline is 5.0, with a standard deviation of 1.33. The shaded areas show two standard deviations above and below the baseline mean (±2.66). Eight consecutive points in the intervention phase fall above this band. Therefore, we would conclude that there was a significant change from the baseline to the intervention phase.

Serial Dependency

It is also possible to use conventional statistical tests, such as the t-test and analysis of variance (see Chapters 19 and 20), with time-series data; however, these applications are limited when large numbers of measurements are taken over time. Under these conditions, data points are often interdependent, as is often the case in single-subject research.^32,33 This interdependence is called serial dependency, which means that successive observations in a series of data points are related or correlated; that is, knowing the level of performance at one point in time allows the researcher to predict the value of subsequent points in the series. Serial dependency can interfere with several statistical procedures, and may also be a problem for making inferences based on visual analysis.^34,35

The degree of serial dependency is reflected by the autocorrelation in the data, or the correlation between data points separated by different intervals, or lags. For example, a lag 1 autocorrelation is computed by pairing the first data point with the second, the second with the third, and so on for the entire series. Using lag 2, the first data point is paired with the third, the second with the fourth, and so on. The higher the value of autocorrelation, the greater the serial dependency in the data. Ottenbacher³ presents a method for computing autocorrelation by hand, but the process is easily performed by computer, especially with large numbers of data points. For further discussion of this analysis, see the section on time series designs in Chapter 10.

C Statistic

The C statistic is a method of estimating trends in time-series data.³⁶ This statistic can be computed with as few as eight observations in a phase, and is not affected by autocorrelation in the data series.³

Calculations begin with baseline data only, to determine if there is a significant trend in Phase A. If there is no significant trend, the baseline and intervention data are combined, and the C statistic is computed again to determine if there is a significant change in trend across both phases. If the baseline data do show a significant trend, the C statistic is less useful.³

The process for calculating the C statistic is illustrated in Tables 12.1A and 12.1B. In this case, the baseline data do not show a significant trend. The combined data, however, do show a significant trend. Therefore, we conclude that there is a difference in performance from baseline to intervention.

Statistical Process Control

Pfadt and colleagues³⁷ introduced a unique application of a statistical model to evaluate variability in single-subject data. This model, called statistical process control (SPC), was actually developed in the 1920s at Bell Laboratories as a means of quality control in the manufacturing process.³⁸ The basis of this process lies in the desire to reduce variation in outcome; that is, in manufacturing, consistency in production is desirable. One can always expect, however, some variation in quality. Cars come off the assembly line with some defects; clothing will have irregularities. A certain amount of variation is random, expected and tolerable. This variation is considered background "noise," or what has been termed common cause variation.²³ Statistically, such variation is considered to be "in control"; that is, the variation is predictable.

There will be a point, however, at which the variation will exceed acceptable limits, and the product will no longer be considered satisfactory for sale; that is, such variation identifies problems in production. Such deviation is considered "out of control," and is called special cause variation. This is variation that is unexpected, intermittent and not part of the normal process. Consider, for instance, the variation in your own signature. If you sign your name 10 times there will be a certain degree of expected or common cause variation, due to random effects of fatigue, distraction or shift in position. If, however, someone comes by and hits your elbow while you are writing, your signature will look markedly different—a special cause variation. We can think of this variation in the context of reliability. How much variation is random error, and how much is meaningful, due to true changes in response?

Applying SPC to Single-Subject Data

We can apply this model to single-subject designs in two ways. First, by looking at baseline data, we can determine if responses are within the limits of common cause variation (expected variability).³⁷ This would allow us to assess the degree to which the data represent a reasonable baseline. Sometimes extreme variability within a baseline can obscure treatment effects.³⁹ We may also find that one point exceeds the limits of common cause, and can be accounted for by special circumstances, thereby discounting the variation as important. For instance, we may find that a patient's responses over the baseline period are consistent except for one day when he did not feel well, or a different clinician took measurements. By analyzing the circumstances of special cause, we can often determine if the response is significant. Consider, for example, the data in Figure 12.5. A steadily decreasing trend is noted during the intervention phase, except for one point on day 9. The concept of special cause obliges the researcher to reflect on possible reasons for this variation.

We can also look at the degree to which intervention responses vary from baseline, with the intent of assigning special cause to the intervention. In other words, we want the treatment to cause a meaningful change in the subject's response. Statistical process control offers a mechanism to determine if variations in response are of sufficient magnitude to warrant interpretation as special cause.²³

Upper and Lower Control Limits

Statistical process control is based on analysis of graphs called control charts. These are the same as the graphs we have been using to show the results of single-subject data, although some differences exist depending on the type of data being measured. The "X-moving range chart" (X-mR)^§ is used with continuous variables, and will be used most often with single-subject data. Other charts should be used when data are binary outcomes or counts.²⁴ Statistical process control charts can be drawn using SPSS^® software under the Graph function.

In SPC, the interpretation of data is based on variability around a mean value. A central line is plotted, representing the mean response for the phase. An upper control limit (UCL) and lower control limit (LCL) are then plotted at 3 standard deviations above and below the mean.^∗∗ Regardless of the underlying distribution, almost all data will fall within ±3 sd from the mean if the data are stable; that is, if the process is in statistical control.⁴⁰ Therefore, these boundaries define the threshold for special cause.^††

Although there is some variability in defining the criteria for special cause, the most common set of rules is:^23,39,40

1. Any one point that falls outside the upper or lower control limits (see Figure 12.15A).

2. Seven or more consecutive points all above or all below the center mean line, called a "run" (see Figure 12.15B).

3. Six or more consecutive points moving up or down across the center mean line, called a "trend" (see Figure 12.15C).

Consider once again the hypothetical data in Figure 12.16. Calculation of the UCL and LCL values are shown in Table 12.2. The baseline data all fall within the upper and lower control limits, demonstrating common cause or chance variation. This is what we would hope to see in a stable baseline. We then extend the control limits into the intervention phase to determine if special cause is present once we have initiated treatment. We can see that 9 points fall outside the UCL, indicating that there is a significant difference in the response during the intervention phase.

As a process for total quality control, SPC can be used within healthcare settings to monitor variation in service delivery and health outcomes. The reader is encouraged to consult several excellent references that discuss this application.^{40,41,42,43,44}

The special appeal of single-subject research is that it focuses on clinical outcomes and can provide data for clinical decision making. With this intent, then, it is not sufficient to demonstrate these outcomes during an experimental period. It is also necessary to show that improvements or changes in behavior will occur with other individuals under conditions that differ from experimental conditions, and will be sustained after the intervention has ended. The term generalization is used in this sense to represent a limited form of external validity for the single case. Although significant effects on a single patient provide no "proof" that a treatment will work for others, it is not unreasonable to assume that the treatment will work for other patients with similar characteristics.

The important contribution of single-subject research is that the specific characteristics of the treatment and the circumstances in which the treatment is successful can be delineated, so that this assumption can be tested. Clinicians can begin to ask questions about which specific patient traits are relevant. In addition, visual inspection of individual performance allows the researcher to observe clinically strong effects that would not necessarily have been statistically significant (and would therefore have been ignored). Therefore, results from single case designs may actually provide more "real world" insight and understanding of individual responses than data from group studies.

Direct Replication

To demonstrate external validity, it is necessary to replicate the results of single-subject experiments across several subjects or by repeating the study on the same subject. This is called direct replication. The setting, treatment conditions, and patient characteristics should be kept as constant as possible. External validity becomes stronger as results accumulate across subjects, establishing what types of patients respond favorably to the treatment. One successful single-subject experiment and three successful replications are considered sufficient to demonstrate that findings are not a result of chance.^45,46 Multiple baseline designs provide direct replication.

Systematic Replication

Systematic replication is used to demonstrate that findings can be observed under conditions different from those encountered in the initial experiment. Systematic replication should occur after generalization across subjects has been established through direct replication. The purpose of systematic replication is to define the conditions under which the intervention will be successful or fail. It is, in essence, a search for exceptions.⁴⁵ It involves the variation of one or two variables from the original study in an attempt to generalize to other similar, but not identical, situations. For instance, the target behavior can be monitored in different settings than the original study; different clinicians, support personnel, or family members can perform the intervention; the treatment may be given at different times of day; or different types of equipment may be used. The continued success of intervention under these changed conditions provides strong evidence supporting application of the treatment under clinical conditions that typically cannot incorporate experimental controls.

For example, in a study of children who suffered from asthma, the children were tested for their ability to use inhalation equipment.⁴⁷ They were given specific rewards for proper use of the equipment within special training sessions, and demonstrated successful learning. It was then of interest to establish that the children could maintain their performance when they were actually exhibiting asthmatic symptoms. To evaluate this generalization, the investigators told the children that the "intervention," the reward strategies, would continue if they used the equipment properly whenever it was really needed. Follow-up data, provided by the nursing staff, supported the generalization of the target behavior to actual treatment situations.

We can also incorporate a follow-up or maintenance phase in a single-subject design, which involves monitoring the target behavior after the intervention is stopped, often weeks or months later. For example, in a study of naming deficits in patients with aphasia, accuracy was assessed at baseline, during intervention, and again at 6 and 10 weeks following completion of the study.⁴⁸ These single measures can be shown on the graphs, indicating the level of retention. Follow-up is important when the intent of treatment is to effect a permanent change in behavior.

Clinical Replication

Although we have attempted to define the process of single-subject research using a clinical model, in reality the fit is less than perfect. Treatment plans are not developed around isolated patient problems, nor are they based on partitioned treatment components. In the long run, then, the true applicability of research data will depend on our ability to demonstrate that treatment packages can be successfully applied to patients with multiple behaviors that tend to cluster together. Barlow and Hersen⁴⁵ have called this process clinical replication. Such a procedure may be considered field testing; that is, clinical replication becomes one with actual practice.

Clinical replication is an advanced replication procedure, which can occur only after direct replication and systematic replication have supplied the researcher with well defined relationships between treatment components and patient characteristics. After testing these relationships one at a time, the researcher can begin to build clinical strategies by combining and recombining successful treatments for coexisting problems. For example, consider the multitude of problems inherent in disorders such as stroke, cerebral palsy, autism, and low back dysfunction. Many of the "treatments" that are used to address these problems incorporate a variety of techniques, with expected overlapping and combined effects. In fact, these treatment programs are not always successful. A comprehensive process of clinical replication is really the only way to establish the conditions under which we can expect positive results.

Social Validation

Beyond the question of external validity, which concerns generalization of findings to different subjects and settings, behavioral analysts are also interested in the importance of treatment effects within a social context. Social validity is based on the significance of the goals of interventions, the acceptability of procedures by target groups, and the importance of the treatment's effect.⁴⁹ These determinations may be made by patients, families or caregivers, or they may be applied within a broader framework by epidemiologists and clinicians.⁵⁰ Social validity is considered important especially with regard to behavior change strategies, to assure that interventions will be appreciated and adopted.

This is a practical issue, based on whether interventions are satisfactory and perceived as useful. Procedures that are intrusive or impractical are less likely to be used, and therefore, less important to study. For example, researchers used a single-subject withdrawal design to study the effect of using therapy balls as seating for young children with autism spectrum disorder on their classroom behavior.⁵¹ The study showed improved behavior, and at the completion of the study, surveys of teachers, staff and parents working with participants showed that they were satisfied with the results and wanted to use the balls for classroom and home seating.

Although social validation is not required for establishing treatment effectiveness, it has always been recognized as an important element of treatment planning and decision making. It serves a valuable function in the interpretation of clinical research findings as evidence for practice. Measures of social validation should be encouraged as a critical link between single-subject research and the treatment planning process.