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Файл:Ординатура / Хирургия / Библиотека им академика М.И. Перельмана / Книга_3091_Библиотеки_им_академика_М_И_Перельмана
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any trial, regardless of the choice of a comparator, participants receive enhanced
care in the form of closer surveillance. Thus, use of the term “enhanced” is justied.
Blind toOutcomes
Blinding investigators to the primary outcome of a clinical trial until all data are
collected and analyzed is standard in clinical trial methodology. The rationale for
this is that if investigators, staff, and/or participants knew of the results of a trial
before it ended, it could limit enthusiasm for completing the trial, encourage partici-
pants to seek out the better treatment, and result in dropouts, non-adherence, and
treatment crossovers. After the last participant completes follow-up, investigators
can be unblinded to the primary outcome, and papers focusing on the primary out-
come can be published.
There is, however, debate on the wisdom of preparing interim reports on secondary
outcomes before the trial has ended. Interim reports are common in medicine. A
review of trials conducted between 2006 and 2015 with “interim” in the abstract
reported that the majority of interim reports were in the areas of oncology, surgery,
and cardiology, they were industry-sponsored, and they were not pre-specied in
the protocol [31]. There is little information about interim reports in behavioral tri-
als, but they appear to be equally, if not more, common. Since participants are aware
of the particular behavioral treatment they are receiving, the risks of reactivity to an
interim report are greater. Any interim reports should be carefully planned ahead of
time with careful consideration of the risk of bias balanced against the importance
of getting such reports out, approved by an independent monitoring committee, and
pre-specied in the trial protocol.
A related question is whether or not interventionists should remain blinded to arm-
specic, aggregated data on behavioral risk factor targets of treatment. For example,
in a Phase III behavioral trial examining the impact of a treatment to reduce anger
on blood pressure control, the behavioral risk factor is anger. If unblinding the inter-
ventionists to lower-than-expected changes in anger during the course of the trial
motivates them to strengthen treatment delivery, it could improve the potency of the
treatment. Alternatively, it could create undesired reactivity such as loss of interest.
This question needs careful consideration by trial investigators since there are cur-
rently no guidelines for blinding to behavioral risk factor targets in Phase III behav-
ioral efcacy trials.
Develop aBlinding Plan
A blinding plan can help investigators push to extend the blind to as many players
as possible. Table10.1 presents an example of a blinding plan using a matrix that
describes potential players and potential blinding options. Within the matrix are
examples of blinding (B) or unblinding (U) options. The goal of the plan is to seek
as many “B’s” as possible in pursuit of making a serious effort to extend the blind.
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These are simply examples. Each trial is different in terms of its scope, resources,
and goals. In planning a trial, investigators might consider developing their own
matrix of players and options. The ultimate decision of who and how to blind
depends upon the nature of the trial and the results of each of the decisions on ethi-
cal issues (i.e., safety), practicality (i.e., feasibility), bias (i.e., how serious the risk
of bias is without blinding), and compromise (i.e., considering options for partial
blinding) [32]. When objective digital outcomes assessment is used, it eliminates
the human middleman and reduces the opportunity for human preferences to create
bias. Consideration must also be made of where in the process of treatment develop-
ment the program of research lies. In earlier phases of treatment development where
resources are limited and the number of players is small, blinding options may be
more limited.
Table 10.1 Sample blinding plan
Blinding Options
Players
Trial
Hypotheses
Trial
Aims
Subject
Treatment
Assignment
Aggregate
Outcomes
Treatment
Fidelity
Intervention
Protocols
Principal
Investigator
U U
B B U U
Co-Investigators
B/U U B B U B/U
Statistician U U U U U
B
Project Director B U B B U U
Interventionists
B U U
a
B U
a
U
a
Research
Assistants
B U B B U B
Participants B U U
a
B U
a
U
a
Participant
Physicians
B U B B B B
Outcome
Assessors
B U B B B B
Institutional
Review Board
U
b
U B B B U
Data Safety and
Monitoring
Board
U U U
c
U U U
U = Unblinded,
B = Blinded
a
Unblinded only within own arm
b
IRB Protocol unblinded; consent form blinded to hypotheses
b
Unblinded in the aggregate only; blinded to individual participants
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Prevent andDetect Expectancy Bias
Differential preferences and absence of equipoise are subtle aspects of the culture of
a clinical trial. They are difcult to document directly but can be inferred indirectly
in a number of ways. In double-blind trials, a common practice is to ask participants
to guess whether they were on active drug or placebo after the trial was completed.
If participants are correct around 50% of the time in a two-arm trial, an inference of
satisfactory blinding can be made [11]. This, of course, is not possible in a behav-
ioral trial because all subjects know which treatment they are on. Here are some
more feasible strategies for preventing and detecting risk of bias in a behavioral trial.
Prevent andDocument Crossovers andCo-interventions
To prevent crossovers and co-interventions during the course of a trial, it is helpful
to educate potential participants at baseline about how clinical trials work and how
beginning new behavioral treatments and/or new lifestyle habits that are unrelated
to the trial can undercut an ability to evaluate results. Once randomized, a thorough
documentation of therapies, treatments, and lifestyle habits at baseline, and repeat-
edly throughout the follow- up, is advisable. This can help assess the possibility that
differential expectations translated into differential co-interventions or crossovers
creating a post-randomization imbalance between arms.
Conict ofInterest
Investigator conict of interest can be an indirect indicator of preference or lack of
equipoise. In biomedical research, conicts have been associated with risk of bias
[33] and statistically signicant results [34]. In biomedical papers published in
2016, 20% reported a conict, but prevalence increased to 32% in the subset of
papers evaluating drug treatments [35]. Conicts of interest are less common in
behavioral trials but could occur when there are nancial interests or a long-stand-
ing scientic commitment to a particular behavioral treatment. In the former case,
transparency through disclosures and funding sources can help assess any inuence
on the integrity of a clinical trial. In the latter case, serious consideration of whether
or not a long- standing interest in a particular behavioral treatment will compromise
objectivity in the design, conduct, and analyses of trial data is essential.
Independent Monitoring
In Phase III efcacy trials, an independent data and safety monitoring board that
monitors trial quality, and a data management center with independent authority to
report on trial progress, provide objective and ongoing feedback to investigators
concerning any evolving imbalances between arms. This maximizes the chance that
such imbalances can be corrected earlier rather than later. For smaller projects, the
principal investigator should work out a written agreement of independence with a
statistician and data manager and report this in all publications as evidence of
extending the blind. The practice of having the principal investigator who directs the
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trial also analyze the data from the trial undercuts the objectivity of the results and
should be avoided. This cannot be justied even by the smallest of budgets.
Assess theRisk ofBias
The Cochrane Collaboration has developed a Risk of Bias scale aimed at determin-
ing the extent of bias after the trial has been completed [36]. It assesses the risk of
expectancy bias based upon metrics that are symptoms: treatment crossovers, dif-
ferential co-interventions, differential attrition, and the subjectivity of the outcomes
[30]. During the trial, use of this instrument can be helpful in the early detection and
early remediation of any emerging biases triggered by differential expectations.
SELECTED EXPERIENCE
FROMBEHAVIORAL TRIALS
“Something or Nothing” inaMulti-Site Behavioral Trial
The ENRICHD clinical trial tested the hypothesis that treatment for depression in
those who were depressed after a new heart attack would reduce subsequent recur-
rent heart attacks or death [37]. The trial, conducted under the direction of the US
National Heart, Lung, and Blood Institute, involved eight sites, a data coordinating
center, a treatment delity center, and a data safety and monitoring board. A total of
2481 post-heart attack patients were randomized to either depression treatment or
usual care. Those randomized to depression treatment received cognitive behavior
therapy, supervised by experts at the Beck Institute where the treatment was devel-
oped. Those randomized to the comparator received usual care. For all patients,
baseline scores on depression were sent to their primary care provider. Results on
the primary endpoint of death or recurrent heart attack after 29months showed no
signicant difference in event-free survival in usual care (75.9%) vs. depression
treatment (75.8%). This was a null trial.
It is often said that “getting something” is better than “getting nothing.” This is a
rationale that drives many community-based studies to resist using randomized com-
parator groups. But in this trial, depressed patients who got a great deal of “some-
thing” (i.e., cognitive behavior therapy for depression supervised by experts) fared
no better than getting “nothing” (i.e., usual care). Because the three authors of this
book were all a part of this trial, we have inside knowledge of the mindsets of the
investigators throughout the progression of the trial. Although the investigators were
kept blinded to outcome data, symptoms of a lack of equipoise were present. For
example, recruiters would come back to staff meetings and express great worry that
a patient who was extremely depressed would end up in the usual care group. Upon
conclusion of all data collection, an investigator unblinding session was scheduled.
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This triggered discussions among the investigators about what the results might look
like. There was not one of the approximately 40 investigators who thought this
would be a null trial. Some measured their enthusiasm by speculating that the inter-
vention would be more effective for recurrent heart attacks than for mortality. Others
speculated that the intervention would prove to be more effective for those who were
more severely depressed. But the predominant view was that getting something,
especially a “something” that was a well-established, efcacious treatment for
patients who needed it, would surely be better than getting nothing. It is safe to say
that a null trial was an unexpected shock. It is also safe to say that this shock revealed
a relatively hidden lack of equipoise on the part of the ENRICHD investigators.
The direction of bias in situations where there is a lack of equipoise is generally in
favor of treatment. The treatment could prove to be superior because of a confound
between its active ingredients and beliefs about its efcacy. In the case of ENRICHD,
it is possible that any lack of equipoise did not translate into a spurious benet for
treatment because its effects were neutralized by the excellent operational proce-
dures put in place by the independent data coordinating center. Early detection of
differential expectancy in the form of monthly reports examining differential drop-
out and non-adherence by arm made it possible for early enhancement of retention
strategies within specic subgroups.
Symptoms ofExpectancy Bias inanObesity
Management Trial
POWeR+ was a behavioral clinical trial aimed at determining the effectiveness and
cost-effectiveness of a web-based behavioral weight management intervention
offered in conjunction with either face-to-face or remote nurse support for patients
managed in primary care [38]. Eligible participants were obese (or overweight if they
had co-morbid hypertension, hypercholesterolemia, or diabetes) who were recruited
from 56 primary care practices in Central and South England. A total of 818 partici-
pants were assigned to one of three arms: a control group of web-based dietary
advice plus 2 brief nurse contacts (N=279), a web-based weight management pro-
gram with face-to-face nurse contacts (N=269), or a web-based weight management
program with remote nurse contacts (N=270). The clinically signicant outcomes
were weight loss averaged over 12months and≥5% weight loss at 12months.
At the 12-month follow-up, weight loss ≥5% was achieved in 21% of the controls,
29% of the face-to-face group, and 32% in the remote group. Statistical signicance
was achieved between the control and remote group only. In a responder-only anal-
ysis, the controls underwent a clinically signicant 3 kg of weight loss. By
12months, 47% of the controls were taking part in a non-trial weight loss activity.
It is rare to see almost half of the participants in a control group in a weight manage-
ment study opting to get weight loss treatment on their own. Widespread treatment
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crossover is a symptom of expectancy bias, but it is difcult to document because
lack of equipoise and preference for a trial outcome is a subtle aspect of the trial
culture. The long-standing interest the investigators had in internet-based programs
such as POWeR+ supports the possibility that expectations prompted treatment
crossover in the controls.
The corrective action of seeking weight management treatment on their own paid
off for the controls in the form of a clinically signicant weight loss. The controls in
this trial underwent more weight reduction (3kg) than they did in an earlier report
(1.2kg) [39]. But what was good for the controls was not necessarily good for the
trial. Treatment crossovers weakened the effect size, undercut statistical power, and
provided an alternative explanation for the failure to detect benet in the face-to-
face group.
The Dream ofa“True Believer”
The Recurrent Coronary Prevention Project (RCPP) was one of the rst behavioral
clinical trials. Conducted in the 1980s, the hypothesis was that reducing Type A
behavior in patients who had already had one heart attack would prevent a recurrent
heart attack. The trial enrolled 862 post-heart attack patients and randomized them
to group counseling to manage heart disease and reduce Type A behavior or to
group counseling to manage heart disease alone. The primary endpoint was death or
recurrent heart attack. At the 3-year follow-up, there was a 44% reduction in the
primary endpoint in the Type A group [40], which was sustained through the next
8years and more powerful than the 30% reduction in heart attack recurrence that
was observed by beta blocker therapy, one of the most popular drugs prescribed
after a heart attack.
This trial was among the rst to demonstrate a connection between the mind and
the body. It gave birth to the eld of behavioral medicine because it showed that the
mind could inuence an objective physical condition in the body such as a recur-
rent heart attack. The principal investigator of the RCPP, Meyer Friedman, was an
established cardiologist who had written a best-selling book, Type A Behavior and
Your Heart, and the phrase “Type A behavior” was used to describe stress in every-
day conversation. A trial of this importance deserved publication in a top medical
journal such as JAMA or the New England Journal of Medicine. Indeed, it was Dr.
Friedman’s dream to get this trial published in one of these two journals. But the
top journals rejected the paper. As the trial biostatistician, Dr. Powell (the rst
author of this book) scrutinized the reviews to identify fatal aws, but they focused
instead on small errors in presentation that were easily correctable. One could not
help but believe that something else was going on. Ultimately, the papers were
published in a less-visible journal. In the years following the RCPP, two other
investigative teams conducted trials using group-based stress reduction treatments
that were modeled after the RCPP and reported similar positive results [41, 42].
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There are likely a variety of explanations for why Dr. Friedman’s papers were not
published in the top medical journals. Maybe he was ahead of the curve, and there
was no community equipoise on the issue of whether or not stress contributed to
recurrent heart attacks. But in addition, Dr. Friedman was widely perceived to be a
“true believer” who had a nancial and personal interest in showing that Type A
behavior was a coronary-prone behavior. Were the RCPP to have been a null trial,
publication problems in top journals may not have existed. But when ndings were
strong with important clinical implications that challenged the status quo for the
optimum treatment of patients recovering from a myocardial infarction, an easy
reason for disbelief among members of the medical community was that the trial
was led by a “true believer” with a vested interest in producing positive results.
Extraordinary claims require extraordinary evidence. In retrospect, it may have
been more convincing if the “true believer” handed over the leadership of the trial
to another investigator who was an expert clinical trialist with no prior association
with the eld of Type A research. Rather than stepping away from the trial com-
pletely, ideal role for Dr. Friedman might have been to be the passionate supervisor
of the Type A intervention arm.
RECOMMENDATIONS
The rigor of a behavioral clinical trial is based upon its strength in making an infer-
ence that a treatment, and not some extraneous confounder, caused an outcome.
Random assignment balances arms at baseline which effectively balances both
known and unknown confounders. But things can happen during the course of the
trial that raise red ags about the continued equality of the randomized arms. This
chapter has argued that one source of post-randomization imbalance is caused by
differential expectations about the benet of treatments being compared and a lack
of equipoise about the expected trial result.
This is a serious problem for behavioral trials because the double-blind design, which
effectively neutralizes the adverse effects of differential expectations, is generally not
possible. Thus, the onus is on the behavioral trialist to maximize rigor by designing
a trial and creating a culture that minimizes bias from differential expectations.
Investigator Discipline
The behavioral trialist faces a perfect storm of three challenges: academic advance-
ment; long-standing commitment to a behavioral treatment; and the human longing
for success. These powerful forces weigh heavily against a scientic mindset char-
acterized by equipoise and freedom from prejudices.
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Investigators must nd the discipline to compartmentalize their mindset. Equipoise
lives in the professional realm. A mindset of true uncertainty about the merits of any
treatment, paired with a passion for a conclusive resolution of this uncertainty,
should be evident in all trial interactions. Hope for a particular trial result is a private
affair. It lives in the personal realm. When hope is brought to the worksite, it
becomes bias. Passion for a trial result is the professional gratication of getting a
conclusive answer to the question posed by the trial. It is reserved for the end of the
road. It is the short leap after the long run.
Such discipline and compartmentalization may be impossible for the trial leader. If
the commitment to, and the passion for, a particular treatment is so strong and long-
standing that a scientic mindset is not possible, the optimum role of such a “true
believer” is to lead the treatment arm, not the trial. To serve as the passionate super-
visor, trainer, and insurer of quality control in the treatment arm would have the
greatest effect on the strength of the treatment and the quality of the trial. The emer-
gence of clinical trial networks and national data coordinating centers makes it more
feasible now than ever before to have a behavioral trial conducted with the highest
quality without having to assume a leadership role.
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Innovate toExtend theBlind
At least 20 scales exist to rate the quality of a clinical trial, and approximately half
of them give points to double-blind designs [43]. The quality of blinding of both
physicians and patients to therapy has been considered to be one of the most impor-
tant aspects of any trial [44]. This means that behavioral clinical trials will always
be rated as trials of lower quality based upon an uncontrollable factor inherent in the
nature of the treatments being evaluated.
This motivates the push to extend the blind in as many ways as possible to make up
for the inability to use double-blind designs. Behavioral clinical trial methodology
is evolving to increase precision about what exactly is meant by “blinding” in any
particular clinical trial. In 2001, CONSORT guidelines for reporting blinding in a
clinical trial were dichotomous reports aimed at determining:
“Whether or not participants, those administering the interventions, and those assessing
outcomes were blinded. If done, how the success of blinding was evaluated.” [45]
In 2010, these guidelines extended the range of possible individuals who could be
blinded and discarded dichotomous reports in favor of open-ended descriptions of
how blinding was accomplished:
“If done, who was blinded after assignment to interventions (e.g., patients, care provid-
ers, those assessing outcomes) and how.” [46]
A deep appreciation of the reality of equipoise and the adverse effects of prefer-
ences for a behavioral trial result can translate into innovations in nding ways to
extend the blind in as many ways, and to as many individuals, as possible. Such
innovations will go far in boosting the rigor of behavioral trials.
Placebo Response: Nuisance Variable or Treatment
Component?
The literature on what constitutes a placebo response and the range of effects it can
produce is evolving. It is now clear that the placebo response is a robust phenome-
non that occurs in a variety of treatments for many diseases in diverse healthcare
settings [47]. In drug trials, a placebo control disentangles improvement in biologi-
cal dysfunction from any improvement triggered by the clinical encounter. An abil-
ity to make this distinction is consistent with the biomedical emphasis on the
science, rather than the art, of medicine.
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But when it comes to behavioral treatments, this distinction is less clear-cut.
Soothing contextual factors such as attention, feeling cared for, and the ritual of
administering the treatment are part of the art of healing and the reduction of symp-
toms [15, 19] with clear physiological benets [18]. Thus, control for non-specic
attention or intervention context may in actuality be overcontrol for an important
component of a behavioral treatment.
It is an open question whether contextual factors produce a placebo response in
need of control, or whether they serve as components of treatment which activate
the “inner pharmacy” of self-healing [15, 48]. The status quo is to assume that these
contextual factors are nuisance variables in need of control with appropriate com-
parators. A major step forward in behavioral clinical trial methodology would be
taken by more in-depth consideration of what are, and what are not, active compo-
nents of a behavioral treatment. This would make it considerably easier to choose
an appropriate comparator for a behavioral trial.
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