This document discusses a study that used advanced regression methods to analyze data from a single-case design clinical trial of propranolol for treating agitation in patients with traumatic brain injury. The study was a double-blind, randomized clinical trial of 13 patients (9 men and 4 women) with traumatic brain injury. Logistic regression models found that propranolol was not associated with less agitation for most participants, though 4 participants did show a significant response. The study demonstrates how single-case design data can be analyzed using regression methods to obtain clinically and statistically significant information about psychological and medical treatments.

1. Advanced Regression Methods for Single-Case Designs: Studying
Propranolol in the Treatment for Agitation Associated With Traumatic
Brain Injury
Daniel F. Brossart
Texas A&M University
Jay M. Meythaler
Wayne State University
Richard I. Parker, James McNamara, and Timothy R. Elliott
Texas A&M University
Objective: The use of single-case designs in intervention research is discussed. Regression methods for
analyzing data from these designs are considered, and an innovative use of logistic regression to analyze
data from a double-blind, randomized clinical trial of propranolol for agitation among persons with
traumatic brain injury (TBI) is used. Method: Double-blind, randomized clinical trial performed in an
outpatient rehabilitation setting. Participants: Nine men and 4 women with TBI. Results: Logistic
models indicated that propranolol was not associated with less agitation for most participants (⌽ ⫽ .135;
90% exact confidence interval was ⫺.03 ⬍ .135 ⬍ .29). Four participants displayed a significant
response to propanolol. Two participants demonstrated significant improvement, and the other 2 expe-
rienced significantly more agitation in the treatment phase. Summary: Advanced regression methods can
be used to analyze data from single-case designs to obtain information of clinical and statistical
significance from a variety of psychological and medical treatments.
Keywords: single-case design, logistic regression, propranolol, brain injury, agitation
In a thoughtful commentary, Aeschleman (1991) observed a
decreasing interest in single-case research (SCR) designs in the
rehabilitation psychology literature: Between 1985 and 1989, Ae-
schleman found only 6 out of 402 empirical papers published in
Rehabilitation Psychology, Archives of Physical Medicine and
Rehabilitation, and Rehabilitation Counseling Bulletin used a sin-
gle-subject design (⬍1.5% of the total; Aeschleman, 1991, p. 43).
A brief examination of the past 15 years of Rehabilitation Psy-
chology reveals one article that offered an innovative way to
analyze single-case data (Callahan & Barisa, 2005) and another
that was a true single-case study (Pijnenborg, Withaar, Evans, van
den Bosch, & Brouwer, 2007).
We disagree with Aeschleman’s bleak conclusion that SCR
designs “. . . have not made a methodological impact on research
in rehabilitation psychology” (Aeschleman, 1991, p. 47). History
informs otherwise: Many of the influential research programs in
rehabilitation psychology first appeared in the literature in single-
case designs. Behavioral approaches—championed in the classic
Behavioral Methods in Chronic Pain and Illness (Fordyce,
1976)—were based on earlier single-case studies. The potential of
supported employment— arguably one of the few evidence-based
practices in rehabilitation psychology with considerable support
from many randomized clinical trials (RCTs; Dunn & Elliott, in
press)— appeared in a study using a single-case case design
published in the Journal of Applied Behavior Analysis (Wehman et
al., 1989). And the ground-breaking extensions of Neal Miller’s
operant learning models to visceral, reflex, and motor responses
were achieved in single-case designs (Brucker & Ince, 1977; Ince,
Brucker, & Alba, 1978). Clearly, SCR designs have played a
pivotal role in the rehabilitation psychology research base.
Unfortunately, SCR and case studies are often misconstrued as
one in the same. An uncontrolled case study is a study of a single
client, dyad, or group in which observations are made under
uncontrolled and unsystematic conditions. The lack of experimen-
tal control in such a study may have contributed to an overall
suspicion or distrust of results based on a single subject in general.
Designs that add more experimental control include systematic,
repeated observations of a single client, dyad, or group and are
often called intensive single-case designs. For even more experi-
mental rigor, one could use a single-case experimental design,
which is typically viewed as having greater control than intensive
single-case designs. These designs usually have behavioral goals or
target behaviors that are the main focus of interest and function as the
dependent variable. They also have repeated measurements over time
and at least two treatment phases (baseline and treatment). Some have
Daniel F. Brossart, Richard I. Parker, James McNamara, and Timothy R.
Elliott, Department of Educational Psychology, Texas A&M University;
Jay M. Meythaler, Department of Physical Medicine and Rehabilitation,
Wayne State University and Rehabilitation Institute of Michigan, Detroit,
Michigan.
This study was funded in part by National Institute of Disability Re-
search and Rehabilitation Grant H 133G000072 awarded to Jay M.
Meythaler. Appreciation is expressed to Michael E. Dunn for sharing
information and opinions about the history of single-case designs in reha-
bilitation psychology research. Graphs of participant data not presented in
this article are available upon request from Daniel F. Brossart.
Correspondence concerning this study should be addressed to Daniel F.
Brossart, Department of Educational Psychology, 4225 TAMU, College
Station, TX, 77845. E-mail: brossart@tamu.edu
Rehabilitation Psychology
2008, Vol. 53, No. 3, 357–369
Copyright 2008 by the American Psychological Association
0090-5550/08/$12.00 DOI: 10.1037/a0012973
357

2. stated that the core essence of single-case research is that “all
dependent measures are collected repeatedly over the course of the
experiment, and these data are not combined with those from other
participants to produce group averages for purposes of data anal-
ysis” (Morgan & Morgan, 2001, p. 122). Nevertheless, there are
also instances in which evaluating single-case data across partic-
ipants is helpful because it can increase the internal validity of the
design.
In this article, we begin by briefly discussing some present
issues, past practice, and some misunderstandings regarding sin-
gle-case research. We then show how the application of single-
case research can be helpful in answering substantive questions.
To illustrate this, we use data collected from a double-blind,
crossover RCT to examine the effectiveness of drug therapy in
reducing agitation in individuals with a traumatic brain injury
(TBI). Furthermore, we introduce a new methodology for analyz-
ing single-case data and compare it with a more traditional regres-
sion method.
Why Consider SCR Now?
Although others have urged for an increased use of single-case
research, such calls for the use of single-case research appear to
have had little effect in changing the behavior of researchers
(Blampied, 2000; Goldfried & Wolfe, 1996; Hilliard, 1993; Mor-
gan & Morgan, 2001). SCR continues to be an underused research
design.
Several forces, however, do appear to be making an impact. One
is the present-day focus on effect sizes. Many journals now require
investigators to report effect size with contextual information for
their interpretation (Fidler, 2002). A similar trend toward account-
ability, objectively measured outcomes, and greater scientific rigor
can be seen in policy statements by influential groups such as the
National Research Council (Shavelson & Towne, 2002). The med-
ical profession’s accountability reform has also played a part in the
movement for the broader use of effect sizes (Oakley, 2002).
Funding agencies, public and private, are increasingly requiring
empirical results and effect sizes. In addition, the call for greater
accountability and objective, defensible results (Shavelson &
Towne, 2002) in psychological and educational research has been
an important factor leading to greater scrutiny of how SCR is
summarized.
Recognizing the Limitations of RCTs
There appears to be an increasing recognition that RCTs are
ideal for answering some research questions but that the design
itself is not able to answer all important questions and that its
implementation has certain limitations. This has led some to con-
tinue to call for both efficacy and effectiveness studies (Tucker &
Roth, 2006). Important questions about how any given single RCT
is conducted and the validity of the results gained have prompted
guidelines for registering RCTs for public scrutiny (Elliott, 2007).
The intention is that this requirement will address deficiencies in
the quality control of RCTs. However, the validity of RCTs are
often compromised in many applications relevant to rehabilitation
psychology by a low number of available participants (with low-
incidence disabilities) and because true control groups are difficult
(if not impossible) to attain due to the lack of services that negate
a “usual treatment” scenario for a controlled, comparison group
(such that any attention to control participants would be above and
beyond the typical experience or “treatment-as-usual”; Elliott,
2007).
The use of single-case designs also helps address the overuse of
cross-sectional methods so common in rehabilitation psychology.
Just as many introductory research design texts talk about the
monomethod bias for a single research study, overuse of a single
design within a field creates a lopsided literature base that lacks the
advantages of triangulation with multiple research methodologies.
Researchers across the health care fields have called for an ex-
panded evidence base, reflected in a broadened focus and a plu-
rality of methodologies to answer questions regarding informed
practice (Concato, Shah, & Horwitz, 2000; Spring et al., 2005).
Single-case designs seem a ready way to add methodological
diversity to the literature base.
SCR Compared With Traditional Cross-Sectional
Research Designs
The more commonly applied cross-sectional research designs
are, in general, nomothetic approaches: They “aim to establish
lawful relations that apply across individuals” (Nesselroade, 1991,
p. 96). Thus, two key characteristics of cross-sectional designs are
“static observations and multiple behavioral categories” (Baltes &
Nesselroade, 1979, pp. 11–12). In contrast, SCR designs may be
seen as a hybrid form of the longitudinal approach. Longitudinal
designs have the ability to identify not only the processes and
causes of intraindividual change but also the processes and causes
of interindividual patterns of intraindividual change in behavioral
development. Although single-case designs may be used to explore
patterns and processes, they typically focus on evaluating the
impact of a treatment on a client, student, or patient. Because
attention is given to collecting data before treatment begins, after
treatment starts, and sometimes even after treatment ends, each
research participant may serve as their own control. Thus, SCR can
be viewed as an alternative methodology for answering many of
the same research questions as cross-sectional group research and
as a methodology that is uniquely capable of answering different
and new research questions.
When Should One Use SCR Designs?
SCR should be considered as a top candidate research design
to use in several circumstances. It is ideally suited for studying
low-incidence problems and conditions. Many behavioral issues
that accompany conditions such as TBI and spinal cord injury
(SCI) are difficult to study in designs that rely on large, repre-
sentative samples for randomization and treatment. For exam-
ple, SCR has been used to study treatments to promote wheel-
chair pushups among men with SCIs (White, Mathews, &
Fawcett, 1989) and other attempts to prevent pressure sores
(Malament, Dunn, & Davis, 1975). These are significant clini-
cal issues that often challenge and confound clinicians; how-
ever, they are not manifested in a sufficient number of individ-
uals required to attract the necessary attention and financial
support for a large-scale (or multisite) RCT.
358 BROSSART, MEYTHALER, PARKER, MCNAMARA, AND ELLIOTT

3. For low-incidence problems, SCR designs are probably one of
the few designs that researchers could use to expand the knowl-
edge base productively in a time-efficient manner. Cross-sectional
designs can take a considerable amount of time to obtain a sample
of sufficient size for data analysis. SCR designs are also indicated
for studies in which few participants are able to meet the inclusion
criteria for a study. In addition, SCR would be beneficial in any
study in which participants are required to participate over an
extended period of time. Such studies often experience a fair
amount of attrition. If an SCR design was used, for the data that
was complete, although possibly much smaller than the number of
participants the study began with, this would still allow important
research questions to be answered. Because each participant serves
as their own control, the existing data would still allow one to
make important inferences (this is not to diminish the import of
considerations one must make when interpreting results with high
levels of attrition). Multiple scenarios are presented in Appendix A
as examples of when SCR should be considered.
Problems With Data Analyses
In spite of the fact that SCR has played an important historical role
in psychology and that there have been a number of replicable
empirical findings in differing domains, Morgan and Morgan (2001)
stated that SCR “remains relatively obscure because of its disavowal
of the statistical machinery that defines psychological research in the
21st century” (p. 120). Furthermore, those involved in SCR have
historically relied on visual analysis (Busk & Marascuilo, 1992;
Kratochwill & Brody, 1978), which Kazdin (1982) defined as the
procedure (largely informal) for reaching a judgment about reliable or
consistent intervention effects by examining graphed data visually.
Indeed, one of the most recent review articles on single-subject
research in rehabilitation failed to acknowledge any of the available
statistical procedures for analyzing data from these designs (Back-
man, Harris, Chisholm, & Monette, 1997).
There is a continued and legitimate need for visual analysis. As
recently noted by Parker, Cryer, and Byrns (2006), visual analysis
plays at least seven important roles in SCR:
(a) to simultaneously consider multiple data attributes in complex
graphs; (b) to identify cycles and other patterns embedded within and
across phases; (c) to distinguish between improvement and deterioration
in effect sizes, and to interpret effect size magnitudes; (d) to validate
whether results (with predictions lines) are meaningful, by being within
score-scale limits; (e) to select the best statistical analysis techniques
from multiple options; (f) to validate the procedures and results from
newer SCR analytic techniques, which lack a track record of successful
published applications; (g) to judge whether SCR datasets meet para-
metric data assumptions (p. 420).
Nevertheless, results on the basis of visual analysis have been
shown to have low reliability even when judges are experienced
professionals, editors of single-case journals, or others provided
with fully contextualized graphs with other design and measure-
ment improvements (Brossart, Parker, Olson, & Mahadevan, 2006;
DeProspero & Cohen, 1979; Harbst, Ottenbacher, & Harris, 1991;
Ottenbacher, 1990; Park, Marascuilo, & Gaylord-Ross, 1990).
Neither technique—visual analysis or statistical analysis—should
be used in isolation: “In single-case research it seems especially
important to investigate how these two methods inform and sup-
port each other” (Brossart et al., 2006, p. 558).
Our own experience highlights the importance of using both
visual and statistical analysis. For example, in previous studies,
we noticed large differences between visual analysis and the
output from ITSACORR (Crosbie, 1993, 1995). Further inves-
tigation showed that ITSACORR was unrelated to other statis-
tical techniques as well as to visual analysis of single-case data
(Brossart & Parker, 2001; Parker & Brossart, 2003), which
raised serious concerns about its viability as a useful technique.
Additional empirical studies have also highlighted its weak-
nesses (Huitema, 2004). It is time for single-case researchers to
abandon the sole use of visual analysis; the dogged refusal to
incorporate statistical analysis of single-case data will simply
result in various fields or lines of research being ignored as
irrelevant, archaic, and unsophisticated.
Some of the underuse of statistical methods has been due to the
cautiousness of researchers in applying univariate parametric anal-
yses because of well-placed concerns that the data fail to meet
assumptions of homogeneity of variance, normality, and serial
independence. In fact, these assumptions are commonly violated
by short, interrupted data series. Even greater concerns have been
voiced about the use of more complex parametric analyses, such as
repeated measures analysis of variance (ANOVA), as it makes
even stronger assumptions of the data (sphericity; Stevens, 2007).
Because of these stringent assumptions, multivariate analysis of
variance (MANOVA) has sometimes been used to replace re-
peated measures ANOVA (RM-ANOVA). However, MANOVA
still has strict assumptions (homogeneity of variance-covariance
matrices, absence of multicollinearity and singularity) and does not
provide output as useful as RM-ANOVA’s partial effect sizes.
For simpler parametric analyses, concerns about unequal variance
and nonnormal distributions are reasonably well addressed by boot-
strapping, a resampling technique that sidesteps data assumptions by
relying on an empirical sampling distribution (Davison & Hinkley,
1997; Good, 2001; Lunneborg, 2000; Simon, 1999). The bootstrap is
attractive and is just beginning to be applied to SCR (Parker, 2006).
Violation of the assumption of serial independence can be addressed
through autoregressive integrated moving average backcasting
(Parker et al., 2006). We take a different approach in the present
article; however, the use of nonparametric analyses is burdened by
only the minimal assumptions of nominal-level data.
Advantages of nominal-level data analysis include its applica-
bility to any SCR data set, regardless of parametric assumptions,
and its greater ease of use, as remedial data transformations are not
needed. The main assumption made by nominal-level data analy-
ses is an adequate sample size for a 2 ⫻ 2 table of about five
expected data points per cell (total N of at least 20–25). All
nominal-level analyses based on the 2 ⫻ 2 table can produce two
effect sizes: (a) Phi (⌽), which is Pearson’s R for a 2 ⫻ 2 table, and
(b) the clinical outcome index, the “risk difference” (medical
terminology), here more appropriately named “improvement rate
difference” (IRD). Given a 2 ⫻ 2 table with balanced marginal
values, these two values are equal (⌽ ⫽ IRD). Standard output for
both indices includes confidence intervals around the obtained
values. For more complex single-case designs, these nominal-level
indices can be obtained through logistic regression (LR).
Other concerns with using statistical analyses on SCR data are
related to the lack of relevance of effect sizes to the traditional
standard of visual analysis (Parsonson & Baer, 1992). An R2
(or R)
effect size derived from ordinary least squares regression and
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SPECIAL ISSUE: SINGLE-CASE RESEARCH

4. interpreted as “percent of variance accounted for” does not re-
sound with more traditional SCR practitioners. A further advan-
tage of nominal-level 2 ⫻ 2 table-based analyses is that they are
based on nonoverlapping data between phases, a keystone of visual
analysis. Depending on the particular method, the approach to
measuring nonoverlapping data varies, but in all cases, the data
overlap can be confirmed visually.
Comparison Method: Simple Mean Shift
(SMS) Regression
Regression models have been used by single-case researchers
since at least 1983 (Gorsuch, 1983). Since that time, many differ-
ent models for analyzing single-case data have been proposed
(e.g., Allison & Gorman, 1993; Center, Skiba, & Casey, 1985–
1986; Faith, Allison, & Gorman, 1996). One of the advantages of
regression models is that they are familiar to many because they
are often covered in doctoral training programs in the behavioral
sciences. They also produce a common effect size, R2
, which can
be converted to other effect sizes such as Cohen’s d (Rosenthal,
1991). Results from individual studies may also be summarized in
meta-analytic studies. Additional advantages include the relative
ease of evaluating power and creating confidence intervals around
the effect size. It is also fairly easy to bootstrap regression models,
especially those models that entail a single step (as opposed to
those that involve multiple steps; e.g., Allison & Gorman, 1993).
Every statistical method has limitations, and one disadvantage
of the regression models is that the effect size, R2
, is not easily
interpreted in terms of treatment effectiveness. Another disadvan-
tage is that there are numerous regression models a single-case
researcher may choose from. Some models try to control for trend
in various ways, some across the entire data series similar to a
covariate in analysis of covariance (e.g., Gorsuch, 1983), others
attempt to control for trend in the baseline phase only (Allison &
Gorman, 1993; Faith et al., 1996). The choice of model depends on
the question the investigator wants to answer. Furthermore, the
effect sizes produced by these regression methods are not directly
comparable to those found in typical cross-sectional regression
studies in terms of the characteristic range and magnitude seen in
SCR. Thus, the interpretive guidelines found in texts by Cohen
(Cohen, 1988), for instance, are of little help in SCR. Investigators
have made some progress in trying to provide tentative interpretive
guidance, but guidelines per se are not available yet (see Brossart
et al., 2006; Parker & Brossart, 2003; Parker et al., 2005). Thus,
the effect size coefficient does not directly communicate the de-
gree of intervention effectiveness.
Among the regression methods available, the one discussed by
Allison and colleagues appears to be one of the more conceptually
and empirically sound options (Allison & Gorman, 1994; Brossart
et al., 2006; Parker & Brossart, 2003). This method involves
multiple steps and effectively controls baseline trend, but it is not
without limitations. Because it controls for baseline trend, the data
series needs to have enough data points to assess trend accurately.
Although one may draw a trend line through three data points, any
baseline based on only three data points should only be analyzed
by a regression method in which mean shift is examined, and even
then such analysis should be considered tentative. More data in
each phase serves to increase the accuracy of any trend line
produced. In addition, because Phase A-predicted values are gen-
erated for Phase B, the technique may infrequently produce values
that extend beyond the range of the dependent variable (on the y
-axis). Such values should be constrained to fit within the limits of
the y-axis variable. An additional limitation of the regression
model promoted by Allison is that one cannot graph the output for
visual analysis. The semipartialing performed by this method
changes the data so much that visual analysis is difficult. Although
trend is removed, graphing the final output does not lend itself
toward a straightforward interpretation. In an effort to improve the
Allison technique, Parker et al. (2006) renamed the technique
mean and slope adjustment (MASAJ) and modified it so that it was
visually interpretable and the question it addressed was slightly
adjusted. The MASAJ technique now answers the question, “What
if phase A trend influence were eliminated or controlled in phase
B?” (Parker et al., 2006, p. 426). In contrast, the Allison technique
answers a similar but different question: “What phase differences
would have been obtained if there had been no phase A trend in the
entire dataset?” (p. 426).
We used a regression model that looks at an SMS between the
baseline and treatment phase for the present study to provide a
comparison to the LR technique. Although it is one of the simplest
models and does not control for baseline trend, we felt it was
important to provide a familiar comparison technique because it is
very different from the LR technique in terms of conceptual
framework and output. This technique was also chosen because a
few data sets contained the treatment drug in the first phase with
the “baseline” or placebo phase following. We deemed it inappro-
priate to use a regression method that controlled for baseline trend
when the treatment phase came prior to the “baseline” phase.
Autocorrelation
In cases in which the investigator chooses to use a regression
technique, it is important to be aware that autocorrelation has been
an enduring problem. Data sets with levels of autocorrelation ⱖ ⫾
.20 may be considered problematic regardless of statistical signif-
icance (Matyas & Greenwood, 1996). The presence of autocorre-
lation violates the assumption of data independence. To remove
autocorrelation, one may use an autoregressive integrated moving
average model with a lag-1 parameter for backcasting rather than
forecasting, as is typically done. The traditional cautions against
using time series analysis for this application do not apply (see
Parker et al., 2006).
Addressing Threats to Validity
Among the strongest (in internal validity) and most flexible
SCR designs is the multiple baseline design (MBD) across
subjects (Kazdin, 1982). The MBD permits an overall judgment
of intervention effectiveness from multiple (typically 3 or 4)
data series. Each data series represents one client. The most simple
data series is AB, that is, a baseline phase followed by an inter-
vention phase. The strength of the MBD is in implementing the
intervention at different times for the clients, thus reducing the
likelihood that the performance change is due to some event other
than the intervention. Increasing the number of clients, each with
staggered intervention onset, improves the control of “history” as
360 BROSSART, MEYTHALER, PARKER, MCNAMARA, AND ELLIOTT

5. an alternative explanation for behavior change (Kazdin, 1982). For
history to be present, the external event would need to impact the
participants concurrently. Any history effect should be seen across
all individuals at approximately the same time. Without such
evidence, the threat of history can usually be ruled out. Maturation
is only a problem in special circumstances in which the length of
the study and the variables measured may, in fact, reflect devel-
opmental changes in the participants.
With MBD, each data series and client are viewed as an inde-
pendent replication, contributing evidence to the omnibus judg-
ment. That judgment is easy to make when improvement is uni-
formly strong across clients, but when results vary, the overall
judgment of intervention effectiveness is more difficult to make.
That problem situation can be handled by calculating effect sizes.
Statistical Methods Have Improved
Recent innovations in SCR include the ability to calculate
effects sizes, in most cases with confidence intervals (Parker et al.,
2005; Parker & Hagan-Burke, 2007b), the use of phase contrasts
(Parker & Brossart, 2006), controlling autoregression, controlling
preexisting baseline trend (Parker et al., 2006), and the use of the
bootstrap (Parker, 2006). In the past 20 years, the number of
analytic techniques available for short data series has easily tripled
since the early 1980s (Barlow & Hersen, 1984; Kazdin, 1982). The
difficulty has been that few studies compared the statistical tech-
niques with each other and with visual analysis. Thus, those who
wanted to use these statistical techniques had little information in
terms of how to interpret the output. Increasingly, researchers have
recognized this deficiency in the literature base and have made
some progress in addressing this need (e.g., Brossart et al., 2006;
Parker & Brossart, 2003). Presently, it appears that effect sizes
vary, depending on the statistical technique used to produce them,
and that the effect size magnitudes produced from cross-sectional
research are very different than those produced from SCR (e.g.,
Parker et al., 2005).
Summary
To summarize, SCR designs should be used because they are
ideally suited to address questions unanswerable by cross-sectional
designs, they address the overuse of cross-sectional designs in the
literature base, and it is no longer the case that there are few
statistical methods to analyze single-case data. In addition, the
MBD is a powerful design that competes well against other de-
signs in terms of internal validity. In the remainder of the present
article, we present a small RCT that can be conceptualized as a
hybrid multiple baseline study. We then analyze these data using
a statistical technique burdened by few assumptions, which is well
suited for SCR.
Illustrative Study
To illustrate the usefulness of SCR and advanced regression
methods for analyzing data from these designs, we examined data
collected from a funded project (awarded to Jay Meythaler) to
conduct a randomized, double-blind, crossover trial of propanolol
with a placebo control among patients who were more than 1 year
postbrain injury (BI).
Agitated behavior after BI can be very disruptive during acute
medical care, inpatient rehabilitation, and in the community. Pre-
vious studies have reported agitated behavior in 11%–34% of
patients with BI in the acute phase (Brooke, Questad, Patterson, &
Bashak, 1992; Levin & Grossman, 1978; Reyes, Bhattacharyya, &
Heller, 1981). Although prevalence rates of agitation in the post-
acute phase are lacking, many patients seen in long-term follow-up
after severe BI demonstrate significant behavioral dyscontrol and
agitation. Such sequelae have a devastating impact on family
relationships and overall functioning, considerably hampering
community reintegration of persons with BI.
Agitation is generally regarded as a disturbed behavioral pattern
often accompanied by overactivity and an “explosive” (i.e., lack-
ing goal direction), impulsive aggression among persons with BI
who have regained cognitive awareness (Corrigan & Mysiw, 1988;
Silver & Yudofsky, 1994). Historically, clinicians have relied on
pharmacological treatments of agitated behavior (Cardenas &
McLean, 1992; Rowland & DePalma, 1995). A recent Cochrane
review of these agents observed that beta-blockers (particularly
propanolol) appear to have the best evidence of effectiveness
(Fleminger, Greenwood, & Oliver, 2006). In spite of such reviews
supporting the use of beta-blockers, a recent survey indicates that
specialists seem to prefer anti-epileptics and atypical antipsychot-
ics (Francisco, Walker, Zasler, & Bouffard, 2007). The mechanism
of action for the anti-aggressive properties of propanolol is essen-
tially unknown, although it is unlikely to be due to propranolol’s
peripheral beta-blocking activity because the doses required to
manage agitated behavior often well exceed the doses required to
saturate fully peripheral beta-adrenergic receptors (Coltart &
Shand, 1970; Yudofsky, Williams, & Gorman, 1981). Propranolol
may likely exert its anti-aggressive properties via central antago-
nism of noradrenergic and serotonergic neurotransmission at sev-
eral subsets of receptors.
For example, both the noradrenergic and serotonergic sys-
tems have been implicated as neurophysiologic substrates of
aggressive behavior in animal studies, though these systems
probably subserve different types of aggressive behavior and
seem to interact in a complex fashion (Cassidy, 1990; Eichel-
man, 1987; Miczek, Weerts, Haney, & Tidey, 1994). The loca-
tions of noradrenergic and serotonergic cell bodies (the locus
ceruleus and dorsal raphe nuclei, respectively), as well as their
neuronal (white matter) projections, are particularly vulnerable
to injury within the brain as a result of acceleration/deceleration
injuries, the most common mechanism of BI (Morrison, Millier,
& Grzanna, 1979; Whyte & Rosenthal, 1993). Because propran-
olol has effects on both beta-adrenergic receptors as well as
serotonin 5-HT1A and 5-HT1B receptors, its apparent effec-
tiveness in managing agitation may be related to modulation of
neurotransmission in these damaged pathways.
However, the Cochrane review noted several problems that
undermine our confidence in the evidence base that merit a closer
scrutiny of propanolol as preferred intervention for agitation. The
reviewers found very few RCTs to evaluate (only six were iden-
tified, generally, in the pharmacological literature), a reliance on
small sample sizes and lack of a systematic reporting of all treated
participants, and no replication studies and a lack of a global
outcome measure to assess the complexity of agitated behavior in
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SPECIAL ISSUE: SINGLE-CASE RESEARCH

6. this population (Fleminger et al., 2006). Although the reviewers
cited the need for further RCTs of the effectiveness of pharmaco-
logical agents, researchers and clinicians were strongly advised to
revisit the use of “N of 1 research methods” to analyze the
effectiveness of the intervention in research projects and in clinical
case management (Fleminger et al., 2006).
As we observed earlier, these clinical realities and methodolog-
ical issues often vex intervention research in rehabilitation. And as
we demonstrate, SCR designs and advanced regression techniques
can be used efficiently to examine the effectiveness of clinical
interventions for grouped data (necessary for RCTs) and for clin-
ical case management (to monitor individual response to treat-
ment). In the remainder of this article, we demonstrate the use and
implications of SCR and regression techniques in a randomized,
double-blind crossover trial of propanolol in the treatment of
agitation among persons with postacute BI.
Method
Twenty individuals with BI who were sequentially enrolled in
an outpatient brain injury clinic were invited to participate in the
present study. Each potential participant and his or her family
members were given a thorough explanation of the study together
with a detailed informed consent document. Every effort was made
to explain the purpose of the study and the risks and benefits of
participation to the potential participant, and to obtain assent or
refusal. For individuals unable to provide informed consent, deci-
sions regarding participation fell to family members or the per-
son’s designated surrogate decision maker.
The inclusion criteria were as follows: (a) BI due to closed or
penetrating head trauma and/or hypoxia greater than 1 year prior to
entry into the study; (b) 14 years of age or older; and (c) a
clinically significant level of agitated behavior, defined as that
which interferes with activities of daily living or independent
living skills. In order to more carefully operationalize the level of
agitated behavior necessary for inclusion, this study relied on the
behavioral ratings by family members on the Agitated Behavior
Scale (ABS; Corrigan, 1989) obtained by the staff member. Pro-
spective individuals qualified for entry into the study if they obtain
at least two scores on the ABS (described in the Measures section)
of 25 or greater in a 2-week period.
The exclusion criteria were as follows: (a1) medical contrain-
dications to initiation of a beta-adrenergic blocker, including a
recent history of congestive heart failure, cardiac arrhythmia, atrio-
ventricular conduction defect (2nd degree or higher), or asthma
requiring pharmacologic intervention; (b) clear medical indica-
tions for prescription of a beta-adrenergic blocker for reasons other
than agitation; (c) demonstrated inability to tolerate propranolol
due to hypotension or bradycardia; (d) suspected development of
increased intracranial pressure requiring neurosurgical interven-
tion (e.g., placement or revision of ventricular-peritoneal shunt).
Participants
The sample available for study consisted of 13 persons with TBI
(4 women, 9 men). Participants who had only two data points in
either the baseline or treatment phase were excluded. The final
sample that was analyzed consisted of 10 participants. Sample
ethnicity consisted of 12 Caucasians and 1 African American. The
average age of the participants was 34 (SD ⫽ 9.78).
Measures
The ABS (Corrigan, 1989) was used to assess agitation. The
ABS is a 14-item scale designed to assess agitation objectively
among persons with TBI. At the end of each observation period,
raters assign a number ranging from 1 (absent ) to 4 (present to an
extreme degree ) for each item, representing the frequency of the
agitated behavior and/or the severity of a given incident. Total
scores range from 14 (no agitation) to 56 (extremely severe agi-
tation). In previous studies, the ABS has demonstrated adequate
reliability and validity (Corrigan, 1989). Factor analysis of the
ABS yielded a three-factor solution: Aggression, Disinhibition,
and Lability (Corrigan & Bogner, 1994).
The initial ABS was completed by a family member in an
interview conducted by Timothy R. Elliott. This was used to
determine sufficient level of agitation to qualify for the study. At
the introductory evaluation prior to randomization, family mem-
bers met with Timothy R. Elliott to learn how they were to assess
agitation each week of participation with the ABS. During this
session, family members were instructed in the use of the ABS. An
instructional videotape (depicting various agitated behaviors) was
played for the family members to rate the depictions of agitation
on the ABS. These ratings were reviewed and critiqued by the staff
member. Family members were given copies of the ABS and
instructed to rate the participant’s agitation each week. Completed
scales were mailed to the research team or returned in subsequent
visits.
Intervention
The study was designed to be a randomized, double-blinded,
crossover trial. Upon enrollment in the study, each participant had
a 2-week observation period during which placebo was adminis-
tered in a single-blind fashion. ABS observations began during this
period. Pharmacy personnel used a double-blind randomization
procedure to assign participants to receive either the active agent
(propranolol) or placebo for the first arm of the study. The study
drug (propranolol or placebo) was prepared by the pharmacy and
delivered to the clinic. A 2-week supply of study drug contained in
a blister pack and labeled with the dosage increment was provided
at each clinic visit.
Participants had pulse and blood pressure checked at each clinic
visit. Dose of the study drug was adjusted to a tolerated dosage
increment for supine blood pressures less than 55 diastolic or 95
systolic in patients under 50 years of age; less than 70 diastolic or
110 systolic in patients 50 years of age and over. Eight participants
were started at an initial dose of 60 mg of long-acting propranolol
(Inderal-LA) per day; 2 participants were started at an initial dose
of 80 mg of propranolol (Participants 4 and 7). Dosages were
increased for participants who demonstrated tolerance for the
preceding dosage. From this protocol, 1 participant received a
maximum dosage of 180 mg (Participant 1), 1 received a maxi-
mum dosage of 120 mg (Participant 8), 6 participants received a
maximum dosage of 80 mg (Participants 3, 4, 5, 6, 7, 10), and 2
were maintained at a dosage of 60 mg (Participants 2 and 9).
Ratings of agitation for each individual were conducted weekly
362 BROSSART, MEYTHALER, PARKER, MCNAMARA, AND ELLIOTT

7. from 6 to 14 weeks (average 10 weeks). Of the 10 clients, 7 were
assessed over 10 or more weeks. The design for each of 9 clients
was a simple AB (baseline period of no treatment, followed by a
treatment period). For 1 participant, the treatment preceded the
baseline period, forming a BA design. Baseline phases ranged
from 3 to 8 data points (mean 5.3 data points), and treatment
phases had the same range (mean 5.1 data points).
Data Analysis
For many research designs, logistic regression (LR) is a close
contender to ANOVA in power and sensitivity, while being bur-
dened with fewer data assumptions (Fox, 2000; Menard, 2002;
Pampel, 2000; Tabachnick & Fidell, 1996). LR is similar to
ordinary least squares (OLS) multiple regression but uses iterative
maximum likelihood estimation (MLE) rather than OLS. Like
multiple regression, LR can use any combination of categorical or
continuous predictors, but the dependent variable must be categor-
ical. LR performs similarly to discriminant function analysis
(DFA), but it is increasingly favored over the latter because of its
fewer data assumptions (Press & Wilson, 1978). Unlike OLS
regression, LR does not assume (a) a linear relationship between
the independent variables and the dependent variable, (b) normally
distributed variables, or (c) equal variance per cell. LR is offered
by most statistics packages, including NCSS (Hintze, 2007), SPSS,
Stata, S-Plus, SYSTAT, and SAS.
Although LR is burdened by few data assumptions, ideally it
needs at least 10 observations for each predictor variable level
(e.g., the smaller Phase A or B; Peduzzi, Concato, Kemper, Hol-
fold, & Feinstein, 1996). In addition, all predictor cells should
have frequencies of at least 1, and no more than 20% of cells
should have less than 5 per cell.
LR does not yield a true effect size but rather one or more
quasi-R2
approximations (e.g., Cox & Snell, 1989; Nagelkerke,
1991). These quasi effect sizes must be interpreted cautiously (e.g.,
they do not represent “percent of variance explained” as do true
R2
s). A second LR output, and the one most important to this
article, is a summary of LR prediction accuracy in a 2 ⫻ 2 table.
LR predicts membership of each data point in either baseline or
intervention phase, based on its relative magnitude. Chance level is
50% accuracy. The 2 ⫻ 2 agreement table, when analyzed by
using chi-square, yields the Pearson’s phi index of association, a
bona fide effect size. Pearson’s ⌽ and ⌽2
are R2
family members,
and familiar to many researchers (Cohen, 1988). Phi also can be
calculated from chi-square: ⌽ ⫽ 冑␹2
/N (where N is the total
number of frequency counts in the 2 ⫻ 2 table).
In a balanced 2 ⫻ 2 table (from LR), phi also can be obtained
by submitting four internal scores to analysis in a “two propor-
tions” statistical module. Phi approximates the difference between
the two proportions and is exactly the same in a balanced table. An
advantage of using a “two proportions” module for analysis is that
it commonly outputs confidence intervals.
In a single-case design, LR analysis requires two predictor
variables, participant and scores, and the dependent measure,
PhaseAB. Though not essential, a fourth serial sequence variable,
time, should be added. Participant is a categorical predictor vari-
able whose number of levels equals the number of clients (data
series) (Levels I, II, III, etc.). Scores serve as a predictor rather
than as a dependent or criterion variable, as is the case with
ANOVA or OLS regression. The dependent variable, PhaseAB, is
dichotomous (Levels A, B). A one-way (noninteraction) model is
specified. The output needed for the present study is only the 2 ⫻ 2
prediction accuracy table, which is ordinarily used for prediction
specificity and sensitivity (involving false negatives and false
positives). Through LR, an attempt is made to predict the phase to
which a score belongs (baseline vs. treatment), based on its size.
The prediction is made on the basis of all participants’ data, but the
classification results also can be disaggregated by individual
participant.
Results
Analysis of the propranolol data set results in a classification
table presented in Table 1. Table 1 indicates that the classification
accuracy for these data is only about chance level, 50%. Any given
data point has an equal chance of belonging to the baseline versus
treatment condition. These results represent an unsuccessful inter-
vention. From a total of 104 data points, only 57% were classified
correctly for phase membership, which is close to chance level.
Submitting this table (only the interior four scores) to a chi-square
analysis yields, ␹2
⫽ 1.9. Phi is output directly as .135 or can be
calculated as, ⌽ ⫽ 冑␹2
/N ⫽ 冑1.9/104 ⫽ .135. Phi can be inter-
preted approximately as “prediction accuracy beyond chance.”
From the 2 ⫻ 2 table, we also can calculate phi from the
difference between two ratios: d/f ⫺ b/e ⫽ 30/51 ⫺ 24/53 ⫽
.5882 ⫺ .4528 ⫽ .135. A two proportions statistical module
provides a 90% exact confidence interval as: ⫺.03 ⬍ .135 ⬍ .29,
and because it spans zero, we note that it could have been obtained
by chance alone. On the basis of all 10 participants, this phi effect
size of approximately .14 indicates the magnitude of change from
baseline to intervention phases for this particular intervention.
Guidelines for interpreting phi magnitudes were recently derived
from 165 analyses of published SCR data (Parker & Hagan-Burke,
2007a). LR results correlated .83 with visual judgments, and
studies judged to show small or negligible results had effect sizes
(interquartile range [IQR]) of .09–.43. Studies judged as showing
medium-size results had effect sizes (IQR) of .53–.72. And studies
judged as showing large results had effect sizes (IQR) of .82–1.0.
This effect size does not indicate whether this change (or lack of
change) can be attributed to the intervention. Attributing change to
the intervention depends on strength of the design. The design of
this example is a multiple-baseline design with 10 independent
client AB data series, and with treatment initiated at 10 different
times. Most single-case researchers would consider this a strong
design. Thus, our hypothesis that participants with agitation would
have a significant reduction in ABS scores on propranolol as
compared with placebo was not supported.
Table 1
Classification Accuracy Table
Actual
Estimated
Total
Baseline Treatment
Baseline 29 24 53
Treatment 21 30 51
Total 50 54 104
Note. Percent correctly classified ⫽ 56.7%.
363
SPECIAL ISSUE: SINGLE-CASE RESEARCH

8. Analyses by Participant
Besides obtaining an index of overall intervention effect, diag-
nostic understanding can be gained from effect sizes for individual
participants. This is accomplished in LR by dropping the partici-
pant predictor variable and entering the data only one participant at
a time. Table 2 includes the 10 effect sizes for the individual
participants, which is compoised of roughly two groups: a larger
group of “little or no effect” (⌽ ⫽ .04, .00, .00, .07, .33, .00) and
a smaller group of “moderate to strong effect” (⌽ ⫽ .52, 1.0, .63,
.87). We include these effect sizes and confidence intervals for the
individual participants because clinicians involved in monitoring
patient progress would focus on each unique client’s progress,
whereas researchers would probably want to distill the results
across multiple baselines in order to determine whether the treat-
ment was effective. Generally, these results indicate that propran-
olol was not effective in lowering agitation for the majority of
participants. The level of analysis one uses depends on the ques-
tion one needs answered.
Comparison to Regression
The results from the SMS regression model conducted on each
participant are included in Table 2. In general, there were three
groups of participants. The largest group contained those partici-
pants that demonstrated no effect while taking propranolol. These
participants obtained R2
values of .02, .07, .04, .05, .22, and .02
and classification rates of 54.5%, 50%, 50%, 54.5%, 66.7%, and
62.5%, respectively. A graphic depiction of the lack of effects
observed for one participant in this group is presented in Figure 1.
Two participants exhibited significantly elevated agitation dur-
ing the propranolol phase (a 33-year-old Caucasian woman and a
37-year-old Caucasian man). We obtained R2
values of .23 and .70
with classification rates of 80% and 83.3%. The small R2
value for
the first participant seems to reflect the nonstatistically significant
phi. Figure 2 depicts the ratings obtained for the 37-year-old man
who exhibited significantly greater agitation on propranolol com-
pared with placebo.
Two other participants displayed significantly less agitation on
propranolol than on placebo (a 51-year-old African American man
and a 23-yearold Caucasian man). We obtained R2
values of .70
and .73 and classification rates of 100% and 92.9%. Figure 3
depicts the significant improvement exhibited by the 51-year-old
man during the propanolol phase.
There were 2 participants who obtained results with R2
values
of .23 and .22. Their classification rates and phi values were
80%, .52 (p ⫽ .10) and 66.7%, .33 (p ⫽ .41), respectively. The
case with the 80% classification rate is rather high, but the phi
value and examination of the confidence interval for the boot-
strapped R2
value, which contains zero, suggest that such a high
classification rate should be interpreted with caution. Interpretabil-
ity would likely be increased if this case had one or two more data
points in the baseline phase, beyond the minimum of three. The
other R2
value of .22 was not associated with a high classification
rate. This data series also obtained a non-significant phi, and the
confidence interval from the bootstrapped R2
also contained zero.
One can more confidently conclude that there is no treatment effect
in these cases.
It is important to emphasize that the interpretation of any sta-
tistical output needs to include visual analysis. These results show
that large effect sizes do not inform one as to the directionality of
the results. This study produced some high-correct classification
rates; however, half those participants did better on propranolol,
and the other half did worse on propranolol.
Discussion
Our main objective in this article was to present a discussion of
advanced regression methods for the analysis of data produced by
SCR. We presented two very different methods, LR and OLS
regression. This is the first attempt that we are aware of in which
investigators have used LR to analyze SCR. The application to a
RCT with multiple-baseline data from a drug study of the effec-
tiveness of propranolol to treat agitation among individuals with
BI was ideal for this demonstration because of the high internal
validity and the multiple data sets available for analysis. Factors
suggesting a high degree of internal validity include multiple-
baseline design, double-blind features, and random assignment to
the ordering of treatment condition. Thus, although the overall
sample size was small, the degree of experimental control for the
present study appears to be rather high.
Our analysis of the multiple-baseline data suggests that overall
propranolol was not an effective treatment for agitation. The effect
size based on these data was .14. This is a small and nonsignificant
effect size and could have been obtained by chance alone. Yet,
when we analyzed participants separately, we found that there
were interesting differences among the participants. Six individu-
als experienced little or no effect on propanolol. Four others
evidenced a moderate to strong effect in response to propranolol:
2 of these participants improved, and the other 2 did worse. The
individual variations in treatment response, which any analysis of
overall group performance cannot address, suggest that agitation
may be influenced by several factors that have yet to be isolated or
understood. The results of our demonstration, then, have implica-
tions for clinical case management and for isolating other variables
in future studies of propanolol in the treatment of agitation.
Clinical scientists are typically interested in their patient’s re-
sponse to treatment. The analysis of each participant’s data sepa-
rately is in line with the clinician’s interest in patient progress. We
can see in these profiles that any particular client’s response may
vary markedly from the overall analysis (which suggested no
effect for the group). As seen in these results, a few participants
had notable results with propranolol. In the absence of contrain-
dications and troublesome side effects, some clinicians may
choose to prescribe propranolol for agitation because it was effec-
tive for some clients. Such a choice would seem to require ade-
quate monitoring to determine whether continued administration
was beneficial, worthwhile, and cost-effective. These observations
are consistent with other expert opinions concerning the use of
propanolol in the treatment of agitation (Fleminger et al., 2006).
There are limitations with the techniques we have demon-
strated in this study. One does not evaluate trends or curves
with LR. In some cases, trend lines or curves may be of primary
interest. In such cases, LR would not be an ideal analytic tool.
LR also has a ceiling limitation. If a treatment obtains a 100%
correct classification rate (a ⌽ of 1), then there is no way in which
to evaluate any magnitude of difference with the technique beyond
the minimum required to obtain the 100% classification rate.
364 BROSSART, MEYTHALER, PARKER, MCNAMARA, AND ELLIOTT

9. Furthermore, additional work remains to determine how this LR
procedure performs with a wide variety of single-case data sets.
Although we have focused on the statistical results, it is impor-
tant to note that the ratings we obtained in this study were not
complicated by patient self-report. The participants were rated by
their family member. Thus, for any participant who improved on
Table 2
Classification Tables for Each Individual Participant
Prt 1: Actual
Estimated
Total Prt 2: Actual
Estimated
Total
Baseline Treatment Baseline Treatment
Baseline 2 1 3 Baseline 7 0 7
Treatment 1 6 7 Treatment 0 5 5
Total 3 7 10 Total 7 5 12
% correctly classified ⫽ 80.0 % correctly classified ⫽ 100.0
␹2
⫽ 2.74, ⌽ ⫽ .52, p ⫽ .097 ␹2
⫽ 12, ⌽ ⫽ 1.0, p ⬍ .001
90% exact C.I. around difference between 2 proportions: ⫺.04 ⬍ .52 ⬍ .86 90% exact C.I. around difference between 2 proportions: .56 ⬍ 1.00 ⬍ 1.00
SMS R2
⫽ .23, bootstrapped Mean SMS R2
⫽ .28, 90% C.I. ⫽ 0, .45 SMS R2
⫽ .70, bootstrapped Mean SMS R2
⫽ .70, 90% C.I. ⫽ .48, .88
Prt 3: Actual
Estimated
Total Prt 4: Actual
Estimated
Total
Baseline Treatment Baseline Treatment
Baseline 1 4 5 Baseline 7 1 8
Treatment 1 5 6 Treatment 1 3 4
Total 2 9 11 Total 8 4 12
% correctly classified ⫽ 54.5 % correctly classified ⫽ 83.3
␹2
⫽ .02, ⌽ ⫽ .04, p ⫽ .89 ␹2
⫽ 4.68, ⌽ ⫽ .625, p ⫽ .03
90% exact C.I. around difference between 2 proportions: ⫺.38 ⬍ .03 ⬍ .46 90% exact C.I. around difference between 2 proportions: .09 ⬍ .63 ⬍ .88
SMS R2
⫽ .02, bootstrapped Mean SMS R2
⫽ .11, 90% C.I. ⫽ 0, .39 SMS R2
⫽ .70, bootstrapped Mean SMS R2
⫽ .70, 90% C.I. ⫽ .45, .89
Prt 5: Actual
Estimated
Total Prt 6: Actual
Estimated
Total
Baseline Treatment Baseline Treatment
Baseline 6 0 6 Baseline 1 5 6
Treatment 1 7 8 Treatment 1 5 6
Total 7 7 14 Total 2 10 12
% correctly classified ⫽ 92.9 % correctly classified ⫽ 50.0
␹2
⫽ 10.5, ⌽ ⫽ .87, p ⫽ .001 ␹2
⫽ 0, ⌽ ⫽ 0, p ⫽ 1.0
90% exact C.I. around difference between 2 proportions: .44 ⬍ .88 ⬍ .99 90% exact C.I. around difference between 2 proportions: ⫺.40 ⬍ .00 ⬍ .40
SMS R2
⫽ .73, bootstrapped Mean SMS R2
⫽ .75, 90% C.I. ⫽ 47, .93 SMS R2
⫽ .07, bootstrapped Mean SMS R2
⫽ .26, 90% C.I. ⫽ 0, .15
Prt 7: Actual
Estimated
Total Prt 8: Actual
Estimated
Total
Baseline Treatment Baseline Treatment
Baseline 1 3 4 Baseline 4 2 6
Treatment 1 3 4 Treatment 3 2 5
Total 2 6 8 Total 7 4 11
% correctly classified ⫽ 50.0 % correctly classified ⫽ 54.5
␹2
⫽ 0, ⌽ ⫽ 0, p ⫽ 1.0 ␹2
⫽ .05, ⌽ ⫽ .07, p ⫽ .82
90% exact C.I. around difference between 2 proportions: ⫺.40 ⬍ .00 ⬍ .40 90% exact C.I. around difference between 2 proportions: ⫺.40 ⬍ .07 ⬍ .53
SMS R2
⫽ .04, bootstrapped Mean SMS R2
⫽ .17, 90% C.I. ⫽ 0, .56 SMS R2
⫽ .05, bootstrapped Mean SMS R2
⫽ .14, 90% C.I. ⫽ 0, .47
Prt 9: Actual
Estimated
Total Prt 10: Actual
Estimated
Total
Baseline Treatment Baseline Treatment
Baseline 2 1 3 Baseline 5 0 5
Treatment 1 2 3 Treatment 3 0 3
Total 3 3 6 Total 8 0 8
% correctly classified ⫽ 66.7 % correctly classified ⫽ 62.5
␹2
⫽ .67, ⌽ ⫽ .33, p ⫽ .41 ␹2
⫽ .00, ⌽ ⫽ .00, p ⫽ 1.0
90% exact C.I. around difference between 2 proportions: ⫺.33 ⬍ .33 ⬍ .81 90% exact C.I. around difference between 2 proportions: ⫺.40 ⬍ .00 ⬍ .54
SMS R2
⫽ .22, bootstrapped Mean SMS R2
⫽ .32, 90% C.I. ⫽ 0, .81 SMS R2
⫽ .02, bootstrapped Mean SMS R2
⫽ .16, 90% C.I. ⫽ 0, .49
Note. Prt ⫽ Participant; C.I. ⫽ confidence interval; SMS ⫽ simple mean shift.
365
SPECIAL ISSUE: SINGLE-CASE RESEARCH

10. propranolol, it may not be necessary for statistical significance to
be achieved. Improved quality of life for the family may be a more
important consideration in some clinical scenarios.
Beyond the findings of this particular study, it should be noted
that with an appropriate measure of outcome and the implemen-
tation of a multiple-baseline design, we presented in this article a
statistical procedure that should be appreciated by peer reviewers
and peer-reviewed outlets. There is no longer an acceptable ratio-
nale for conducting SCR without statistical analysis. Single-case
studies that feature a strong rationale, a multiple-baseline design,
and appropriate statistical analyses deserve a place in the eviden-
tiary foundation of rehabilitation psychology research. With all the
key elements in place, any reluctance to publish such a study
probably reflects editorial bias more than a scholarly critique.
In many respects, the present controversies and needs in our
research make for an exciting time for single-case researchers.
New statistical methods continue to be developed and refined. No
longer must the single-case researcher rely solely on visual anal-
ysis: Regression methods such as those presented here provide two
powerful yet very different methods for analyzing single-case data.
In conjunction with visual analysis, it is hoped that those who may
have previously avoided SCR will now see new avenues for
productive inquiry that can improve clinical practice, enrich the
literature base, and improve the quality of life for consumers of
rehabilitation services.
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368 BROSSART, MEYTHALER, PARKER, MCNAMARA, AND ELLIOTT

13. Appendix A
Scenarios In Which Single-Case Research Designs are Useful
Sample or Client Characteristics
1. When participants are few and/or uniquely different, so pooling together may obscure important differences.
2. When clients are atypical, so are not well represented in normative samples of standardized assessments.
3. When clients have limited response repertoires or low attention abilities, so standardized assessment procedures are of questionable validity.
Clinical or Research Issue
1. When one extensive assessment may have doubtful validity, and periodic, shorter probes would be more credible.
2. When participant performance shows considerable variability over time, from day-to-day or week-to-week.
3. When short-term and medium-term client improvements are of interest and expected.
4. When the concern is about the process of learning or development, styles, etc., rather than outcomes alone.
5. When formative evaluation data are needed to inform further development of an intervention or program.
6. When the amount, intensity, or type of intervention can be varied to an optimum level to better meet individual client needs.
7. When participants are likely to respond to an intervention at different rates, or with different trajectories, curves, profiles, etc.
8. When the focus is on typical daily performance rather than on capacity or aptitude, e.g., habits, addictions, tolerances, social interactions,
lifestyle, routines.
9. When the “ecological validity” of measurement is very important.
10. When events or behaviors over the recent past are important, and yet their recall retrospectively would be inaccurate.
11. When the interest is in the relationship between two behavioral measures over time (cross-correlation).
12. When the interest is in the sequence of behavioral measures over time (lag-sequential conditional probability analysis).
13. When the interest is in contingent relationships between events and behaviors over time (ordinal contingency analysis).
14. When atypical results (e.g., amount of improvement or qualitative pattern of improvement) from individual subjects could be washed out in group
comparisons.
Appendix B
Within NCSS 2007, select Analysis, Regression/Correlation,
Logistic Regression. Enter phase variable as dependent variable
and the variable for treatment score as Numeric Independent
Variable (assuming it is continuous). Under the Response Analysis
Section in the output, you will find the % Correctly Classified, look
in the row titled Total, for the overall % of correctly classified data
points. In the output under the section titled Classification Table
are the values you will enter into the Proportions –Two Indepen-
dent analysis, which is listed under Analysis, Proportions. Make
sure you enter the values from the classification table correctly into
the cells for the proportions test. Select Difference in the Statistics
box and Exact (although a Bootstrap is available) in the Confi-
dence Intervals box. The output will list the Phi under the column
titled Estimated Value, and the confidence intervals will be listed
next to it. Using the Confidence Intervals tab, one may set the
range of the confidence intervals the program produces. One may
also use the Chi-square Effect Size Estimator found under Anal-
ysis, Descriptive Statistics, Contingency Tables. When the classi-
fication table is entered in the cell boxes, the program produces the
chi-square, effect size (Phi), and the probability level. Following
these directions should give one all the necessary output to report
one’s results.
Received December 31, 2007
Revision received June 3, 2008
Accepted June 5, 2008 䡲
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