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component parts: the clinically signicant rate of adherence in the treated and the
expected range of adherence in the controls. The clinically signicant rate of adher-
ence in the treated was xed at the guideline goal of 70% (the green line). The
expected rate of adherence in the controls was estimated, from the literature, to
range between 20% and 40% (the x-axis horizontal line). Included in this calcula-
tion was a curve for a treatment effect of 60% adherence (blue hashed line). This
inclusion was based upon the argument that if treatment improved adherence, but
not to a clinically signicant level, an ability to detect this statistically would
encourage further optimization of the treatment to achieve a clinically signicant
benet. The resulting choice of sample size (30 per group) made it possible to insure
both clinical and statistical signicance if the treatment effect was as low as 60%
and the control effect was as high as 40%.
Clinical Versus Statistical Signicance inPhase III
Efcacy Trials
ENRICHD was a multi-site behavioral trial aimed at, among other things, reducing
depression after a myocardial infarction (MI) for the purpose of reducing cardiovas-
cular recurrence (death or recurrent MI) [46]. The trial compared a treated arm that
received cognitive behavior therapy for depression, to an arm receiving usual care,
in 2481 post-MI patients. This sample size was based upon a two-sided test,
alpha= 0.05, power = 80%, and a 3-year estimated MI event rate of 18% in the
treated and 23% in usual care. Treatment for depression continued for 6months,
after which patients were followed for an average of 23 additional months to accu-
mulate MI events. To achieve benet on the primary outcome, the target for depres-
sion remission was the clinically signicant goal of ≤7 on the Beck Depression
Inventory (BDI), a goal established by experts in depression.
This was a null trial. In the presence of null ndings, it is incumbent upon the prin-
cipal investigators to determine what happened. Such post hoc analyses are explor-
atory and not conclusive. They do, however, provide insight into a reasonable next
step in the program of research.
Figure 5.7 examines change in depression over the duration of the follow-up. At the
conclusion of the 6-month treatment, there was a discrepancy between statistical
and clinical signicance. There was a statistically signicant difference between
treated and controls (p< 0.001); however, the treated patients did not achieve the
clinically signicant threshold of BDI ≤7 either at 6months or at any other time
over the follow-up. Figure5.8 dichotomizes patients from the treated arm only into
those who did and did not achieve the clinically signicant threshold on depression
and compares them on the primary endpoint of cardiovascular recurrence. Relative
to those who failed to achieve the depression threshold (the bar on the left with the
hazard ratio set as the referent at 1.0), those who did achieve the depression thresh-
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old had a 33% lower chance of cardiovascular recurrence (the bar on the right,
hazard ratio=0.66), after adjusting for factors that differed between these groups at
baseline (p<0.01).
The ENRICHD investigators interpreted their results based upon statistical
signicance:
“ENRICHD achieved signicant improvements in depression . . .yet did not demonstrate
a parallel benet on mortality and recurrent infarction.” [46]
An accompanying editorial placed greater emphasis on the discrepancy between the
statistical and clinical ndings:
“The impact on depression scores, although statistically signicant (p<.001) was only
between 1.5 and 2.8 points, depending upon the scale used. . . . A statistically signicant
difference with a small effect size has unclear clinical importance . . . Depression remains
a CAD risk factor in search of a successful intervention.” [47]
But despite this discrepancy, the title of the editorial “Depression—A Cardiac Risk
Factor in Search of a Treatment” suggests that cognitive behavior therapy was not
the right treatment, and the editorial goes on to suggest that exercise, SSRI’s, or
omega-3 supplementation might be more promising [47].
This is an excellent example of the importance of clinical signicance relative to sta-
tistical signicance. Since the sample size of the trial was based upon an ability to
detect a difference on the primary outcome of cardiovascular recurrence, it was con-
siderably overpowered to detect a statistical difference between arms on depression.
The resulting direction of the bias is that very small differences can turn out to be
highly statistically signicant. In contrast, clinical signicance is independent of sam-
ple size. When clinical signicance is considered, the picture changes and it is clear
18
16
14
12
10
8
6
0612 18 24
Treatment
Months
*** p<0.001
***
Usual Care
Treatment
Clinically
Significant Goal
ENRICHD:
Change in Depression
Beck Depression
Fig. 5.7 Clinically vs. statistically signicant
change in depression in ENRICHD
1.2
0.8
0.6
0.4
0.2
0
1
Clinically Non-Significant
(Beck>7)
**p<0.01
ENRICHD:
Primary Endpoint By Clinically Significant Change
1.0
0.66**
Clinically Significant
(Beck≤7)
Hazard Ratio
Fig. 5.8 Primary endpoint in the treated
arm by clinically signicant change in
depression in ENRICHD
Selected Experience fromBehavioral Trials
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that the cognitive behavior therapy approached, but did not achieve, its goal on remis-
sion of depression. It would be informative to examine the treatment delity data in
pursuit of nding ways to strengthen the treatment. This may be a more reasonable
next step than seeking a new treatment for depression. Since the depression treatment
failed to achieve a clinically signicant remission of depression, the hypothesis that
reduction in depression reduces cardiovascular recurrences was not tested. This was
an inconclusive trial. Replication with a stronger depression treatment is needed.
Prioritizing statistical over clinical signicance is common in behavioral trials. In the
Women’s Health Initiative, the largest behavioral trial ever supported by the National
Institutes of Health, 48,835 postmenopausal women free of cardiovascular disease at
baseline were randomized to a dietary intervention or an education comparison group
and followed for an average of 8.1years for a primary endpoint of cardiovascular
events [48]. The clinically signicant dietary target was ≤20% of energy intake from
fat and≤7% energy intake from saturated fat. This was a null trial. With such a large
sample, statistical signicance was easily achieved at year 6 on fat intake between the
treated and comparator arms (p<0.001), but the treated arm fell short of the clinically
signicant goal and achieved 28.8% energy intake from fat and 9.5% energy intake
from saturated fat. Unplanned post hoc analyses showed that those who achieved the
lowest intake of saturated fat had a signicant benet on cardiovascular disease
(p=0.001). Nonetheless, the conclusion in the Abstract of the trial suggested that
statistical signicance was prioritized over clinical signicance:
“Over a mean of 8.1 years, a dietary intervention that reduced total fat intake . . . did not
signicantly reduce the risk of CHD, stroke, or CVD in postmenopausal women . . .”
The intervention did not reduce total fat intake to clinically signicant levels. This
was a failure of the intervention to hit its goal on fat intake, not a failure of the
hypothesis that reduced fat intake and reduced risk of cardiovascular events. But if
the intervention had hit the clinically signicant target, it may very well have trans-
lated into reduced risk on cardiovascular events. The only way to know is to do the
trial again with a stronger intervention.
RECOMMENDATIONS
The essential question of interest to a behavioral trialist is:
“Does this behavioral treatment improve a chronic disease outcome?”
Statistical signicance alone will not provide an answer. When nature is the disinter-
ested nal arbiter, as it is with a chronic disease outcome, it is clear that this “emperor
is not wearing much.” To answer this essential question, recommendations include
interpreting results from behavioral trials with a progressive set of questions.
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Does theTreatment Achieve aClinically Signicant Benet?
The rst question in evaluating the results of a behavioral trial is whether the treat-
ment achieved a clinically signicant benet. Prioritization of clinical signicance
insures that improving health is the end game. Early identication of how strong a
behavioral treatment needs to be in order for it to reduce the risk of chronic disease,
and judging the strength of the behavioral treatment against this criterion, applies to
all stages of behavioral treatment development and all outcomes used at these vari-
ous stages.
A subtle way that clinical signicance is undervalued in clinical trial design is the
pervasive use of an effect size to estimate a treatment’s efcacy on a primary end-
point. This ignores the important question of whether or not the treatment was strong
enough to move a clinical endpoint and judges a treatment’s strength instead by how
it stacks up against the unpredictable response of a comparator group. Effect sizes
should be disaggregated, and separate estimates for treated and comparator groups
should be built into the design, analyses, and interpretation of behavioral trials.
Does theTreatment Achieve aBetter Response than
aComparator?
If the treatment has achieved a clinically signicant benchmark, this justies going
to a second question of Why? or Compared to what? The answer to this second
question is meaningless when the rst question is answered in the negative. If a
treatment does not improve health, a reasonable direction would be to strengthen the
treatment rather than studying its comparative advantage.
An answer to this second question draws on statistical analyses to quantify what
“better” means. Statisticians are intensifying their arguments against statistical sig-
nicance being a substitute for scientic importance. They are in active rebellion
against what they believe has become a tyrant. This is shown in the strength of their
words [12, 13].
“Never use ‘no difference’ or ‘no association’ based upon a p-value.
Statistically signicant—don’t say it and don’t use it.”
Nowhere is it more important to reduce reliance on statistical signicance than in
the eld of applied behavioral clinical trials. Overreliance on statistical signicance
has impeded progress by creating false security about the conclusiveness of nd-
ings, providing a convenient substitute for scientic conclusions, a lack of interest
in replication, and, if a replication is conducted, an inability to reproduce the nding.
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A statistical comparison between a treatment and a comparator provides a useful
metric for quantifying the certainty that exists, contingent upon assumptions, that
there is a true difference between them. To answer the question of the comparative
advantage of the treated relative to the comparator, the actual p-value and condence
interval should be reported along with a thoughtful discussion of the uncertainty
they imply. This is in keeping with best practices in statistics and is consistent with
the uncertainty that is implicit in the use of these statistical tools. Reporting actual
p-values and condence intervals is far superior to the false security implied by the
dichotomous decision that the nding is “statistically signicant” because the
p-value is less than 0.05 or the condence interval does not include 1.
What Is theScientic Conclusion fromThis Trial?
The word “signicance” is confus-
ing. It applies to both the descrip-
tion of the importance of a scientic
conclusion (e.g., a “signicant”
nding) and to the statistical results
(e.g., a “signicant” result). A sig-
nicant scientic conclusion from
a behavioral trial emerges from the
integration of a variety of types of
evidence, of which clinical signi-
cance (i.e., strength of a treatment
to move a clinical endpoint) is at
the top of the ladder and statistical
signicance (i.e., probability of a
result under the null hypothesis) is
closer to the bottom [29].
Because of the confusion surround-
ing the word “signicant,” and the
judgment it implies, it may be wise
to stop using it altogether and
replace with the specic scientic
conclusion drawn from a trial. The
criteria for making a scientic con-
clusion in a behavioral trial are pre-
sented in the box. To arrive at a
rigorous and thoughtful scientic
conclusion from a single behav-
ioral trial, spend less time with sta-
tistical software and more time thinking [13].
Basis for Scientic Conclusions
QUALITY OF THE TRIAL
• Accuracy of assumptions in sam-
ple size calculations made for:
– Treatment effect
– Comparator effect
– Estimate of variability
– Drop-out rate
– Non-adherence rate.
• Protection of randomization
• Freedom from bias
SCIENTIFIC CONTRIBUTION
• Treatment produces a clinically
signicant benet on the primary
outcome
• The certainty of the difference
between the treated and compar-
ator is quantied
• Consistency with results from
similar trials
• Biological plausibility
• Cost relative to benet
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How Conclusive Is theEvidence That This Treatment
Improves Health?
One trial alone is suggestive, but
not conclusive, evidence for the
hypothesis that a behavioral treat-
ment can improve health. Although
there is an extensive literature
aimed at correcting the misinter-
pretation that a statistically signi-
cant result provides conclusive
evidence that a treatment works,
the misinterpretation is nonetheless
sustained for many reasons. Among
them are the seductive thrill of victory, the frustration with getting replications
funded because they are not that innovative, and the fear that any victory is short-
lived in the face of the high risk of inability to replicate.
Replications of results in new trials may not be “innovative,” but they are essential
to the progression of science. Although it is often assumed that the Diabetes
Prevention Project [49] was, unto itself, a denitive test of lifestyle treatment to
prevent the development of diabetes, it was not alone. Replications were conducted
in Japan [50–52], Scandinavia [53], China [54], Europe [55], India [56], and
Finland [57].
The best way for science to approach a conclusive determination of whether or not
a treatment actually works is through replication. In the context of behavioral trials,
reviews of grant proposals and papers should eliminate the criterion of innovation
to judge the scientic contribution. This could make investigators less concerned
about innovation and more concerned about getting to the essential goal of nding
behavioral treatments that actually work.
It is also helpful to have patience
and a healthy dose of humility.
Elizabeth Barrett-Connor, the pro-
lic and inspirational epidemiolo-
gist and clinical researcher, was a
believer in the scientic method.
She reminded her mentees repeat-
edly of it with her words (see box).
Be open.
One study is rarely enough.
“The words ‘groundbreaking new study’
might be loved by news writers but must be
resisted by researchers. Breaking ground is
only the rst step in building a house. It will
be suitable for habitation only after much
more hard work.” [12]
“The only reason to have a hypothesis is
to try to disprove it. If you can’t, you might
be right—not guaranteed to be right, but
you might be right.”
Elizabeth Barrett-Connor
(1935-2019)
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L. H. Powell et al., Behavioral Clinical Trials for Chronic Diseases,
https://doi.org/10.1007/978-3-030-39330-4_6
Chapter 6
The Choice of a
Comparator
The choice of a comparator in a behavioral trial is often based upon implicit rules
that sustain the status quo. In many cases, this status quo is a “one-size-ts-all”
comparator that controls for non-specic treatment factors. The recent emergence
of frameworks for comparator choice aims to create explicit rules which place a
priority on the primary purpose of the trial within its developmental context. This
chapter reviews implicit and explicit criteria for making decisions about an opti-
mum comparator and presents two new frameworks that facilitate decision-making:
the Pragmatic Model for Comparator Selection in Health-Related Behavioral Trials;
and the Purpose-Guided Trial Design Framework. Both encourage an evolution of a
trial’s purpose as understanding of a behavioral treatment progresses, prioritize pur-
pose over logistic and scientic limitations of any particular comparator, and raise
caution about the danger of choosing a comparator that inadvertently changes the
purpose of the trial.
“I would rather have questions that can’t be answered
than answers that can’t be questioned.”
Richard Feynman
Nobel Prize in Physics, 1965
Fundamental Point
The choice of a comparator is one of the most important decisions in the
design of a behavioral trial. It should be driven by the primary research
question that the trial is intended to answer. A comparator that is chosen on
any other basis may leave that question unanswered.
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