The investigator’s ethical
responsibility to the study participants demands that safety and
clinical benefit be monitored during trials. If data partway
through the trial indicate that the intervention is harmful to the
participants, early termination of the trial should be considered.
If these data demonstrate a clear definitive benefit from the
intervention, the trial may also be stopped early because
continuing would be unethical to the participants in the control
group. In addition, if differences in primary and possibly
secondary response variables are so unimpressive that the prospect
of a clear result is extremely unlikely, it may not be justifiable
in terms of time, money, and effort to continue the trial. Also,
monitoring of response variables can identify the need to collect
additional data to clarify questions of benefit or toxicity that
may arise during the trial. Finally, monitoring may reveal
logistical problems or issues involving data quality that need to
be promptly addressed. Thus, there are ethical, scientific, and
economic reasons for interim evaluation of a trial [1–3]. In order to
fulfill the monitoring function, the data must be collected and
processed in a timely fashion as the trial progresses. Data
monitoring would be of limited value if conducted only at a time
when all or most of the data had been collected. The specific
issues related to monitoring of recruitment, adherence, and quality
control are covered in other chapters and will not be discussed
here. The monitoring committee process has been described in detail
[4] as have case studies
representing trials, which were terminated for benefit, harm, or
futility [5]. One of the earliest
discussions of the basic rationale for data monitoring was included
in a report of a committee initiated at the request of the council
advisory to the then National Heart Institute and chaired by
Bernard Greenberg [3]. This report
outlined a clinical trial model depicted in Fig. 16.1, variations of which
have been implemented widely by institutes at the National
Institutes of Health (NIH). The key components are the Steering
Committee, the Statistical and Data Coordinating Center, the
Clinics, and the Data Monitoring Committee. Later the
pharmaceutical and device industries [6] adopted a modified version of this NIH model,
depicted in Fig. 16.2. The main modification was to separate the
Statistical Data Coordinating Center into a Statistical Data
Analysis Center and a Data Coordinating Center. Many of the early
experiences have been described and formed the basis of current
practice [7–34], particularly in trials of cardiovascular
disease [35–37]. Over the past decade especially, the number
of DMCs has increased dramatically [38]. In 2013, of over 120,000 trials registered
in Clintrials.gov, more than 13,000 were interventional trials and
40% of those included a DMC. This suggests over 5,000 DMCs are or
have existed in this period of time. The highest DMC utilization
was in cardiovascular and oncology trials. Of the 630 trials that
were NIH sponsored, 74% had a DMC. For the 55% that were industry
sponsored, about a third had a DMC. Some of this difference is
reflected in the written policies or guidelines by the NIH and the
FDA. The Office of Inspector General (OIG) issued a report in 1998
that reviewed the adequacy of IRB oversight in clinical trials and
recommended that the NIH and the FDA provide guidance on when a
more focused monitoring committee might be needed. In response, NIH
issued a policy statement that was consistent with their
longstanding practice in many of their institutes of having an
independent DMC for all Phase III randomized trials that they
funded [39]. Soon after, the FDA
began to develop a guidance document that was issued as a draft in
2001 and finalized in 2006 [40].
The FDA guidance recommended DMCs for trials with high risk
patients or high risk or novel interventions, not all Phase III or
IV trials conducted by industry.
Fig.
16.1
The NIH Clinical Trial Model
Fig.
16.2
The Industry Modified Clinical Trial Model
[6]
Prior to the year 2000, the general
public was generally not aware of the longstanding practice of data
monitoring committees providing oversight to Phase III trials
especially. However, the death of a gene transfer patient at a
leading research institution changed that [41]. While this patient was not in a Phase III
trial, the issues surrounding the case drew attention as to who was
responsible for monitoring trials and to whom or what body should
such monitoring be reported to. The proximity of this event in time
with the NIH and FDA guidance certainly enhanced public awareness
and DMC activity came under increased scrutiny by a variety of
interested parties. The US Secretary of Health and Human Resources
became aware of these events and also reaffirmed the policies and
practices of the NIH and the FDA [39, 40,
42]. It has also become clear that
for large multicenter trials, an individual IRB, often deluged by
sporadic SAEs from the sponsor, is not able to ascertain if there
is compelling evidence of risk or benefit based on accumulating
data according to (often blinded) treatment in the trial. Thus,
that critical role in assuring patient safety can only be played by
the DMC.
While all trials need some level of
monitoring, many trials such as early phase trials, single center
trials, a very simple intervention trial or a trial not involving
vulnerable populations, may not need an external monitoring
committee. External monitoring, using an independent committee, is
used mostly in later phase trials that could lead to change in
clinical practice or where special expertise is needed. A survey of
monitoring practices conducted by the DAMOCLES group found that the
roles of monitoring committees varied widely across trials,
sponsors, and regions. While there was a general agreement about
the types of trials that needed formal monitoring committees, there
was not a uniform practice or policy as to their function
[43]. External monitoring
committees go by a variety of names such as data and safety
monitoring board (DSMB), data and safety monitoring committee
(DSMC) or simply Data Monitoring Committee (DMC). In this text, we
prefer using DMC since it does not focus on safety when in fact the
challenge is to review the risks and the benefits of a new
intervention.
The principles and fundamentals
expressed in this book reflect the experience of the authors in
monitoring numerous trials since the early 1970s.
Fundamental Point
During the trial, response variables need to
be monitored for early dramatic benefits or potential harmful
effects or futility. Monitoring should be done by a person or group
independent of the investigator.
Monitoring Committee
Keeping in mind the scientific,
ethical, and economic rationales, data and safety monitoring is not
simply a matter of looking at tables or results of statistical
analysis of the primary outcome. Rather, it is an active process in
which additional tabulations and analysis are suggested and evolve
as a result of ongoing review. Monitoring also involves an
interaction between the individuals responsible for collating,
tabulating, and analyzing the data. For single center studies, the
monitoring responsibility could, in principle, be assumed by the
investigator. However, he may find himself in a difficult
situation. While monitoring the data, he may discover that the
results trend in one direction or the other while participants are
still being enrolled and/or treated. Presumably, he recruits
participants to enter a trial on the basis that he favors neither
intervention nor control, a state of clinical equipoise
[44]. Knowing that a trend exists
may make it difficult for him to continue enrolling participants.
It is also difficult for the investigator to follow, evaluate, and
care for the participants in an unbiased manner knowing that a
trend exists. Furthermore, the credibility of the trial is enhanced
if, instead of the investigator, an independent person monitors the
response variable data. Because of these considerations, we
recommend that for later phase trials the individuals who monitor a
clinical trial have no formal involvement with the participants or
the investigators, although some disagree [11, 19,
20].
Except for small, short-term studies
which could be early or late phase, when one or two knowledgeable
individuals may suffice, the responsibility for monitoring response
variable data is usually placed with an independent group with
expertise in various disciplines [4–6]. The
independence protects the members of the monitoring committee from
being influenced in the decision-making process by investigators,
participants as well as federal or industry sponsors. The committee
would usually include experts in the relevant clinical fields or
specialties, individuals with experience in the conduct of clinical
trials, epidemiologists, biostatisticians knowledgeable in design
and analysis, and often for NIH funded trials a bioethicist or
participant advocate. While we will describe statistical procedures
that are often helpful in evaluating interim results in Chap.
17, the decision process to continue,
terminate a trial early, or modify the design is invariably complex
and no single statistical procedure is adequate to address all
these complexities. Furthermore, no single individual is likely to
have all the experiences and expertise to deal with these issues.
Thus, as was recommended in the Greenberg Report [3], we suggest that the independent monitoring
committee have a multidisciplinary membership.
The first priority of the monitoring
committee must be to ensure the safety of the participants in the
trial. The second priority is to the investigators and the
Institutional Review Boards or ethics committees, who place an
enormous trust in the monitoring committee both to protect their
participants from harm and to ensure the integrity of the trials.
Third, the monitoring committee has a responsibility to the sponsor
of the trial, whether it be federal or private. Finally, the
monitoring committee provides a service to the drug or device
regulatory agency, especially for trials which are utilizing drugs,
biologics or devices which still have investigational status.
Although many formats for monitoring
committee meetings have been used, one that we recommend allows for
exchange of information by all relevant parties and for appropriate
confidential and independent review [4, 13]. The
format utilizes an open session, a closed session, and an executive
session. The open session enables interaction between investigator
representatives such as the study principal investigator or chair,
the sponsor, the statistical center, the relevant industrial
participants, and the monitoring committee. It is uncommon but
permissible for a regulatory agency to participate in an open
session of the meeting. In this session, issues of participant
recruitment, data quality, general adherence, toxicity issues, and
any other logistical matter that may affect either the conduct or
outcome of the trial are considered in a blinded fashion. After a
thorough discussion, the monitoring committee would go into a
closed session with DMC members and the statistical reporting
statistician or team where analyses of the confidential unblinded
outcome data are reviewed. This review would include comparison by
intervention groups of baseline variables, primary or secondary
variables, safety or adverse outcome variables, adherence measures
for the entire group, and examinations of any relevant subgroups.
Following this review, the monitoring committee may decide to move
into an executive session with DMC members only where decisions
about continuation, termination or protocol modification are made.
After the DMC review has been completed in closed sessions, they
may meet with a representative of the sponsor or investigator
leadership to share their recommendations which are usually
followed up in a letter. Regardless of how formal, most monitoring
committee meetings have such components. One variation is that the
DMC meeting begins with a closed session which allows the members
to discuss any issues that they want to raise with the
investigators and sponsors in the subsequent open session. This
discussion may also serve to identify what issues will be central
in the second closed session. Thus, the sequence is closed
executive, open, closed and ending with an open debriefing session.
This particular model, for example, has been used extensively in
NIH-sponsored AIDS trials [13].
Before a trial begins and the first
monitoring committee meeting is scheduled, it must be decided
specifically who attends the various sessions, as outlined above.
In general, attendance should be limited to those who are essential
for proper monitoring. As noted, it is common for the study
principal investigator and sponsor representatives to attend the
first open session. If he or she does not provide care for
participants in the trial, the principal investigator will
sometimes attend the closed session; however, that practice is not
recommended. If the study is sponsored by industry, independence
and credibility of the study is best served by no industry
attendance at the closed session. Industry sponsored trials that
are also managed and analyzed by industry will require a
biostatistician from the sponsor who prepares the monitoring report
to attend. In such situations the company statistician must have a
“firewall” separating her from other colleagues at the company,
something that may be difficult to achieve in a way that is
convincing to outsiders. However, a common practice for
industry-sponsored pivotal Phase III trials is for a separate
statistical analysis center to provide the interim analyses and
report to the independent monitoring committee [6]. This practice reduces the possibility or
perception that interim results are known within the industry
sponsor, or the investigator group. Regulatory agency
representatives usually do not attend the closed session because
being involved in the monitoring decision may affect their
regulatory role, should the product be submitted for subsequent
approval.
An executive session should involve
only the voting members of the monitoring committee, although the
independent statistician who provided the data report may also
attend. There are many variations of this general outline,
including a merger of the closed and executive session since
attendance may involve the same individuals.
Most monitoring committees evaluate
one, or perhaps two, clinical trials. When a trial is completed,
that monitoring committee is dissolved. However, as exemplified by
cancer and AIDS, ongoing networks of clinical centers conduct many
trials concurrently [11,
13, 18–20,
23]. Cancer trial cooperative
groups may conduct trials across several cancer sites, such as
breast, colon, lung or head, and neck at any given time, and even
multiple trials for a given site depending upon the stage of the
cancer or other risk factors. The AIDS trial networks in the United
States have likewise conducted trials simultaneously in AIDS
patients at different stages of the disease. In these areas,
monitoring committees may follow the progress of several trials. In
such instances, a very disciplined agenda and a standardized format
of the data report enhance the efficiency of the review. If there
is a research program of several trials evaluating a new drug, a
common DMC may have the advantage of being able to monitor a larger
combined experience that will provide for more precise estimates of
safety and efficacy. Regardless of the model, the goals and
procedures are similar.
Another factor that needs to be
resolved before the start of a trial is how the intervention or
treatment comparisons will be presented to the monitoring
committee. In some trials, the monitoring committee knows the
identity of the interventions in each table or figure of the
report. In other trials, for two interventions the tables may be
labelled as A and B with the identity of A and B remaining blinded
until the DMC requests the unblinding on a “need to know” basis.
Thus, if there are no trends in either benefit or harm, which is
likely to be the case early in a trial, there is no overwhelming
reason to know the identity of groups A and B. When trends begin to
emerge in either direction, the monitoring committee should have
full knowledge of the group identities [45].
In some trials, the monitoring
committee is blinded throughout the interim monitoring. In order to
achieve this, data reports have complex labeling schemes, such as A
versus B for baseline tables, C versus D for primary outcomes, E
versus F for toxicity, and G versus H for various laboratory
results. While this degree of blinding may enhance objectivity, it
may conflict with the monitoring committee’s primary purpose of
protecting the participants in the trial from harm or unnecessary
continuation. As pointed out by Whitehead [46], the intention of this approach is to deny
the DMC a complete picture of the interim data. To assess the
progress of the trial, the harm and benefit profile of the
intervention must be well understood and the possible tradeoffs
weighed. If each group of tables is labeled by a different code,
the committee cannot easily assess the overall harm/benefit profile
of the intervention, and thus may put participants at unnecessary
risk or continue a trial beyond the point at which benefit
outweighs risks. Such complex coding schemes also increase the
chance for errors in labeling. This practice is not common and not
recommended.
No simple formula can be given for how
often a monitoring committee should meet. The frequency may vary
depending on the phase of the trial [2, 4,
5, 47]. Participant recruitment, follow-up, and
closeout phases require different levels of activity. Meetings
should not be so frequent that little new data are accumulated in
the interim, given the time and expense of convening a committee.
If potential toxicity of one of the interventions becomes an issue
during the trial, special meetings may be needed. In many long-term
clinical trials, the monitoring committees have met regularly at 4-
to 6-month intervals, with additional meetings or telephone
conferences as needed. In some circumstances, an annual review may
be sufficient. However, less frequent review is not recommended
since too much time may elapse before a serious adverse effect is
uncovered. As described later, another strategy is to schedule
monitoring committee meetings when approximately 10, 25, 50, 75,
and 100% of the primary outcomes have been observed, or some
similar pattern. Thus, there might be an early analysis to check
for serious immediate adverse effects with later analyses to
evaluate evidence of intervention benefit or harm. Other approaches
provide for additional in-between analyses if strong, but as yet
non-significant trends emerge. Between committee meetings, the
person or persons responsible for collating, tabulating, and
analyzing the data assume the responsibility for monitoring unusual
situations which may need to be brought to the attention of the
monitoring committee.
A monitoring committee often reviews
the data for the last time before the data file is closed, and may
never see the complete data analysis except as it appears in the
publication. There is currently no consistent practice as to
whether a monitoring committee meets to review the final complete
data set. From one perspective, the trial is over and there is no
need for the committee to meet since early termination or protocol
modification is no longer an option. From another perspective, the
committee has become very familiar with the data, including issues
of potential concern, and thus may have insight to share with the
investigators and study sponsors. Some trials have scheduled this
final meeting to allow the monitoring committee to see the final
results before they are presented at a scientific meeting or
published.
Based on our experience, we strongly
recommend this latter approach. There is a great deal to be gained
for the trial and the investigators at a very modest cost. Other
remaining issues still need to be resolved. For example, if a
worrisome safety trend or a significant finding is not reported
clearly or at all in the primary publication, what are the
scientific, ethical, and legal obligations for the monitoring
committee to comment on what is not reported? Suppose the committee
differs substantially in the interpretation of the primary or
safety outcomes? What is the process for resolving differences
between it and the investigators or sponsor? These are important
questions and the answers are not simple or straightforward, yet
are relevant for science and ethics.
Repeated Testing for Significance
In the discussion on sample size
(Chap. 8) the issue of testing several
hypotheses was raised and referred to as the “multiple testing”
problem. Similarly, repeated significance testing of accumulating
data is essential to the monitoring function has statistical
implications [48–54]. These issues are discussed in more detail
in Chap. 17 but the concept of repeated
testing is described here. If the null hypothesis, H 0, of no difference
between two groups is, in fact, true, and repeated tests of that
hypothesis are made at the same level of significance using
accumulating data, the probability that, at some time, the test
will be called significant by chance alone is larger than the
significance level selected in the sample size computation. That
is, the rate of incorrectly rejecting the null hypothesis, or
making a false positive error, will be larger than what is normally
considered acceptable. Trends may emerge and disappear, especially
early in the trial, and caution must be used.
In a clinical trial in which the
participant response is known relatively soon after entry, the
difference in rates between two groups may be compared repeatedly
as more participants are added and the trial continues. The usual
test statistic for comparing two proportions used is the chi-square
test or the equivalent normal test statistic. The null hypothesis
is that the true response rates or proportions are equal. If a
significance level of 5% is selected and the null hypothesis,
H 0, is tested
only once, the probability of rejecting H 0 if it is true is 5% by
definition. However, if H
0 is tested twice, first when one-half of the data are
known and then when all the data are available, the probability of
incorrectly rejecting H
0 is increased from 5 to 8% [50]. If the hypothesis is tested five times,
with one-fifth of the participants added between tests, the
probability of finding a significant result if the usual statistic
for the 5% significance level is used becomes 14%. For ten tests,
this probability is almost 20%.
In a clinical trial in which long-term
survival experience is the primary outcome, repeated tests might be
done as more information becomes known about the enrolled
participants. Canner [10]
performed computer simulations of such a clinical trial in which
both the control group and intervention group event rates were
assumed to be 30% at the end of the study. He performed 2,000
replications of this simulated experiment. He found that if 20
tests of significance are done within a trial, the chance of
crossing the 5% significance level boundaries (i.e., Z = ±1.96) is, on the average, 35%.
Thus, whether one calculates a test statistic for comparing
proportions or for comparing time to event data, repeated testing
of accumulating data without taking into account the number of
tests increases the overall probability of incorrectly rejecting
H 0 and claiming
an intervention effect. If the repeated testing continues
indefinitely, the null hypothesis is certain to be rejected
eventually. Although it is unlikely that a large number of repeated
tests will be done, even five or ten can lead to a
misinterpretation of the results of a trial if the multiple testing
issues are ignored.
A classic illustration of the repeated
testing problem is provided by the Coronary Drug Project (CDP) for
the clofibrate versus placebo mortality comparison, shown in
Fig. 16.3
[10, 54]. This figure presents the standardized
mortality comparisons over the follow-up or calendar time of the
trial. The two horizontal lines indicate the conventional value of
the test statistic, corresponding to a two-sided 0.05 significance
level, used to judge statistical significance for studies where the
comparison is made just one time. It is evident that the trends in
this comparison emerge and weaken throughout, coming close or
exceeding the conventional critical values on five monitoring
occasions. However, as shown in Fig. 16.4, the mortality curves
at the end of the trial are nearly identical, corresponding to the
very small standardized statistic at the end of the
Fig. 16.3. The monitoring committee for this trial
took into consideration the repeated testing problem and did not
terminate this trial early just because the conventional values
were exceeded.
Fig.
16.3
Interim survival analyses comparing
mortality in clofibrate- and placebo-treated participants in the
Coronary Drug Project. A positive Z value favors placebo
[9]
Fig.
16.4
Cumulative mortality curves comparing
clofibrate- and placebo treated participants in the Coronary Drug
Project [9]
For ethical, scientific, and economic
reasons, all trials must be monitored so as not to expose
participants to possible harm unnecessarily, waste precious fiscal
and human resources, or miss opportunities to correct flaws in the
design [2–5]. However, in the process of evaluating interim
results to meet these responsibilities, incorrect conclusions can
be drawn by overreacting to emerging or non-emerging trends in
primary, secondary or adverse effect outcomes. In general, the
solution to multiple testing is to adjust the critical value used
in each analysis so that the overall significance level for the
trial remains at the desired level. It has been suggested that a
trial should not be terminated early unless the difference between
groups is very significant [2,
4, 5, 55]. More
formal monitoring techniques are reviewed in the next chapter,
Chap. 17. They include the group sequential
methods and stochastic curtailed sampling or conditional power
procedures.
Decision for Early Termination
There are five major valid reasons for
terminating a trial earlier than scheduled [2, 4,
5, 9, 10]. First,
the trial may show serious adverse effects in the entire
intervention group or in a dominating subgroup. Second, the trial
may indicate greater than expected beneficial effects. Third, it
may become clear that a statistically significant difference by the
end of the study is improbable, sometimes referred to as being
futile. Fourth, logistical or data quality problem may be so severe
that correction is not feasible or participant recruitment is far
behind and not likely to achieve the target. Fifth, the question
posed may have already been answered elsewhere or may no longer be
sufficiently important. A few trials have been terminated because
the sponsor decided the trial was no longer a priority but this
causes serious ethical dilemmas for investigators and leaves
participants having contributed without getting an answer to the
posed question.
For a variety of reasons, a decision
to terminate a study early must be made with a great deal of
caution and in the context of all pertinent data. A number of
issues or factors must be considered thoroughly as part of the
decision process:
- 1.
Possible differences in prognostic factors between the two groups at baseline.
- 2.
Any chance of bias in the assessment of response variables, especially if the trial is not double-blind.
- 3.
The possible impact of missing data. For example, could the conclusions be reversed if the experience of participants with missing data from one group were different from the experience of participants with missing data from the other group?
- 4.
Differential concomitant intervention and levels of participant adherence.
- 5.
Potential adverse events and outcomes of secondary response variables in addition to the outcome of the primary response variable.
- 6.
Internal consistency. Are the results consistent across subgroups and the various primary and secondary outcome measures? In a multicenter trial, the monitoring committee should assess whether the results are consistent across centers. Before stopping, the committee should make certain that the outcome is not due to unusual experience in only one or two centers.
- 7.
In long-term trials, the experience of the study groups over time. Survival analysis techniques (Chap. 15) partly address this issue.
- 8.
The outcomes of similar trials.
- 9.
The impact of early termination on the credibility of the results and acceptability by the clinical community.
Some trials request the chair of the
monitoring committee to review frequently serious adverse events,
by intervention, to protect the safety of the participants. While
such frequent informal, or even formal, review of the data is also
subject to the problems of repeated testing or analyses, the
adjustment methods presented are typically not applied. Also,
safety may be measured by many response variables. Rather than
relying on a single outcome showing a worrisome trend, a profile of
safety measures might be required. Thus, the decision to stop a
trial for safety reasons can be quite complex.
The early termination of a clinical
trial can be difficult [2,
9, 10, 12,
55–60], not only because the issues involved may be
complex and the study complicated but also because the final
decision often lies with the consensus of a committee. The
statistical methods discussed in the next chapter are useful guides
in this process but should not be viewed as absolute rules. A
compilation of diverse monitoring experiences is available
[5]. A few examples are described
here to illustrate key points. One of the earlier clinical trials
conducted in the United States illustrates how controversial the
decision for early termination may be. The University Group
Diabetes Program (UGDP) was a placebo-control, randomized,
double-blind trial designed to test the effectiveness of four
interventions used in the treatment of diabetes [61–64]. The
primary measure of efficacy was the degree of retinal damage. The
four interventions were: a fixed dose of insulin, a variable dose
of insulin, tolbutamide and phenformin. After the trial was
underway, study leaders formed a committee to review accumulating
safety data. This committee membership consisted of individuals
involved in the UGDP and external consultants. The tolbutamide
group was stopped early because the monitoring committee thought
the drug could be harmful and did not appear to have any benefit
[64]. An excess in cardiovascular
mortality was observed in the tolbutamide group as compared to the
placebo group (12.7% vs. 4.9%) and the total mortality was in the
same direction (14.7% vs. 10.2%). Analysis of the distribution of
the baseline factors known to be associated with cardiovascular
mortality revealed an imbalance, with participants in the
tolbutamide group being at higher risk. This, plus questions about
the classification of cause of death, drew considerable criticism.
Later, the phenformin group was also stopped because of excess
mortality in the control group (15.2% vs. 9.4%) [61]. The controversy led to a further review of
the data by an independent group of statisticians. Although they
basically concurred with the decisions made by the UGDP monitoring
committee [61], the debate over
the study and its conclusion continued [63]. This trial certainly highlighted the need
for an independent review of the interim data to assess
safety.
The decision-making process during the
course of the CDP [65] a long-term
randomized, double-blind, multicenter study that compared the
effect on total mortality of several lipid-lowering drugs (high-
and low-dose estrogen, dextrothyroxine, clofibrate, nicotinic acid)
against placebo has been reviewed [5, 9,
54, 65, 66]. Three
of the interventions were terminated early because of potential
adverse effects and no apparent benefit. One of the issues in the
discontinuation of the high dose estrogen and dextrothyroxine
interventions [65, 67] concerned subgroups of participants. In some
subgroups, the interventions appeared to cause increased mortality,
in addition to having a number of other adverse effects. In others,
the adverse effects were present, but mortality was only slightly
reduced or unchanged. The adverse effects were thought to more than
outweigh the minimal benefit in selected subgroups. Also, positive
subgroup trends in the dextrothyroxine arm were not maintained over
time. After considerable debate, both interventions were
discontinued. The low dose estrogen intervention [66] was discontinued because concerns over major
toxicity. Furthermore, it was extremely improbable that a
significant difference in a favorable direction for the primary
outcome (mortality) could have been obtained had the study
continued to its scheduled termination. Using the data available at
the time, the number of future deaths in the control group was
projected. This indicated that there had to be almost no further
deaths in the intervention group for a significance level of 5% to
be reached.
The CDP experience also warns against
the dangers of stopping too soon [9, 54]. In the
early months of the study, clofibrate appeared to be beneficial,
with the significance level reaching or exceeding 5% on five
monitoring occasions (Fig. 16.3). However, because of the repeated testing
issue described earlier in this chapter, the decision was made to
continue the study and closely monitor the results. The early
difference was not maintained, and at the end of the trial the drug
showed no benefit over placebo. It is notable that the mortality
curves shown in Fig. 16.4 do not suggest the wide swings observed in
the interim analyses shown in Fig. 16.3. The fact that
participants were entered over a period of time and thus had
various lengths of follow-up at any given interim analysis,
explains the difference between the two types of analyses. (See
Chap. 15 for a discussion of survival
analysis.).
Pocock [55] also warns about the dangers of terminating
trials too early for benefit, reflecting on a systematic review of
trials stopped early [59]. At an
early interim analysis, the Candesartan in Heart failure Assessment
of Reduction in Mortality and Morbidity (CHARM) trial
[68] had a 25% mortality benefit
(p < 0.001) from
candesartan compared to a placebo control, but for a variety of
reasons the trial continued and found after a median of 3 years of
follow-up only a 9% nonsignificant difference in mortality.
Continuing the trial revealed that the early mortality benefit was
probably exaggerated and allowed other long-term intervention
effects to be discovered. In general, trials stopped early for
benefit often do not report in sufficient detail the rationale for
early termination and often show implausibly large intervention
effects based on only a small number of events [57]. This phenomenon is well recognized
[58]. Thus, while there are sound
ethical reasons to terminate trials early because of benefit, these
decisions must be cautioned by our experience with early trends not
being reliable or sustainable. Nevertheless, there is a natural
tension between getting the estimate of treatment benefit precise
and allowing too many participants to be exposed to the inferior
intervention [57]. Statistical
methods to be described in the next chapter are useful as
guidelines but not adequate as rules and the best approach based on
experience is to utilize a properly constituted monitoring
committee, charged with weighing the benefits and risks of early
termination.
The Nocturnal Oxygen Therapy Trial was
a randomized, multicenter clinical trial comparing two levels of
oxygen therapy in people with advanced chronic obstructive
pulmonary disease [69,
70]. While mortality was not
considered as the primary outcome in the design, a strong mortality
difference emerged during the trial, notably in one particular
subgroup. Before any decision was made, the participating clinical
centers were surveyed to ensure that the mortality data were as
current as possible. A delay in reporting mortality was discovered
and when all the deaths were considered, the trend disappeared. The
earlier results were an artifact caused by incomplete mortality
data. Although a significant mortality difference ultimately
emerged, the results were similar across subgroups in contrast to
the results in the earlier review.
Early termination of a subgroup can be
especially error prone if not done carefully. Peto and colleagues
[71] have illustrated the danger
of subgroup analysis by reporting that treatment benefit in ISIS-2
did not apply to individuals born during a certain astrologic sign.
Nevertheless, treatment benefits may be observed in subgroups which
may be compelling. An AIDS trial conducted by the AIDS Clinical
Trial Research Group (ACTG), ACTG-019 [5, 6,
13] indicated that zidovudine
(AZT) led to improved outcome in participants who had a low
laboratory value (CD4 cell counts under 500, which is a measure of
poor immune response). The results were not significant for
participants with a higher CD4 value. Given previous experience
with this drug, and given the unfavorable prognosis for untreated
AIDS patients, the trial was stopped early for benefit in those
with the low CD4 cell count but continued in the rest of the
participants.
A scientific and ethical issue was
raised in the Diabetic Retinopathy Study, a randomized trial of
1,758 participants with proliferative retinopathy [72, 73]. Each
participant had one eye randomized to photocoagulation and the
other to standard care. After 2 years of a planned 5 year
follow-up, a highly significant difference in the incidence of
blindness was observed (16.3% vs. 6.4%) in favor of
photocoagulation [74]. Since the
long-term efficacy of this new therapy was not known, the early
benefit could possibly have been negated by subsequent adverse
effects. After much debate, the monitoring committee decided to
continue the trial, publish the early results, and allow any
untreated eye at high risk of blindness to receive photocoagulation
therapy [75]. In the end, the
early treatment benefit was sustained over a longer follow-up,
despite the fact that some of the eyes randomized to control
received photocoagulation. Furthermore, no significant long-term
adverse effect was observed.
The Beta-Blocker Heart Attack Trial
provided another example of early termination [76, 77]. This
randomized placebo control trial enrolled over 3,800 participants
with a recent myocardial infarction to evaluate the effectiveness
of propranolol in reducing mortality. After an average of a little
over 2 years of a planned 3 year follow-up, a mortality difference
was observed, as shown in Fig. 16.5. The results were
statistically significant, allowing for repeated testing, and
would, with high probability, not be reversed during the next year
[77]. The data monitoring
committee debated whether the additional year of follow-up would
add valuable information. It was argued that there would be too few
events in the last year of the trial to provide a good estimate of
the effect of propranolol treatment in the third and fourth year of
therapy. Thus, the committee decided that prompt publication of the
observed benefit was more important than waiting for the marginal
information yet to be obtained. This trial was one of the early
trials to implement group sequential monitoring boundaries
discussed in the next chapter and will be used as an example to
illustrate the method.
Fig.
16.5
Cumulative mortality curves comparing
propranolol and placebo in the Beta-Blocker Heart Attack Trial
[75]
Another example of using sequential
monitoring boundaries is found in chronic heart failure trials that
evaluated different beta blockers. Common belief had been that
administering a beta-blocker drug to a heart failure patient would
cause harm, not benefit. Fortunately, early research suggested this
belief may have been in error and ultimately four well designed
trials were conducted to evaluate the risks and benefits. Three
trials were terminated early because of beneficial intervention
effect on mortality of 30–35% [78–80]. The
fourth trial [81] did not go to
completion in part due to the fact that the other three trials had
already reported substantial benefits. Details of monitoring in one
of the trials, the Metoprolol CR/XL Randomized Trial In Chronic
Heart Failure (MERIT-HF) are discussed more fully in Chap.
17.
Some trials of widely used
interventions have also been stopped early due to adverse events.
One classic example comes from the treatment of arrhythmias
following a heart attack. Epidemiological data showed an
association between the presence of irregular ventricular
heartbeats or arrhythmias and the incidence of sudden death,
presumably due to serious arrhythmias. Drugs were developed that
suppressed such arrhythmias and they became widely used after
approval by the drug regulatory agency for that indication. The
Cardiac Arrhythmia Suppression Trial (CAST) was a multicenter
randomized double blind placebo-controlled trial evaluating the
effects of three such drugs (encainide, flecainide, moricizine) on
total mortality and sudden death [82]. Statistical procedures used in CAST to
address the repeated testing problem [83, 84] are
described in the next chapter. However, the encainide and
flecainide arms of the trial were terminated after only 15% of the
expected mortality events observed because of an adverse effect (63
deaths in the two active arms vs. 26 deaths in the corresponding
placebo arms).
At the first monitoring committee
review, the mortality trend in CAST began to appear but the number
of events was relatively small [83]. Because the monitoring committee decided no
definitive conclusion could be reached on the basis of so few
events, it elected to remain blinded to the treatment assignment.
However, before the next scheduled meeting, the statistical center
alerted the committee that the trends continued and were now
nearing the CAST monitoring criteria for stopping. In a conference
call meeting, the monitoring committee became unblinded and learned
that the trends were in the unexpected direction, that is, toward
harm from the active treatment. A number of confirmatory and
exploratory analyses were requested by the monitoring committee and
a meeting was held a few weeks later to discuss fully these
unexpected results. After a thorough review, the monitoring
committee recommended immediate termination of the encainide and
flecainide portions of the trial [83]. Results were consistent across outcome
variables and participant subgroups, and no biases could be
identified which would explain these results. The third arm
(moricizine) continued since there were no convincing trends at
that time, but it too was eventually stopped due to adverse
experiences [85]. The CAST
experience points out that monitoring committees must be prepared
for the unexpected and that large trends may emerge quickly. Even
in this dramatic result, the decision was not simple or
straightforward. Many of the issues discussed earlier were covered
thoroughly before a decision was reached [83].
Not all negative trends emerge as
dramatically as in the CAST. Two other examples are provided by
trials in congestive heart failure. Yearly mortality from severe
congestive heart failure is approximately 40%. The Prospective
RandOmized MIlrinone Survival Evaluation (PROMISE) [36] and the Prospective RandOmized FlosequInan
Longevity Evaluation (PROFILE) [35] trials evaluated inotropic agents (milrinone
and flosequinone). Both of these drugs had been approved by
regulatory agencies for use on the basis of improved exercise
tolerance, which might be considered a surrogate response for
survival. PROMISE and PROFILE were randomized placebo controlled
trials comparing mortality outcomes. Both trials were unexpectedly
terminated early due to statistically significant harmful mortality
results, even after adjusting for repeated testing of these data.
Because severe heart failure has a high mortality rate and the
drugs were already in use, it was a difficult decision how long and
how much evidence was needed to decide that the intervention was
not helpful but was in fact harmful. In both trials, the monitoring
committees allowed results to achieve statistical significance
since a negative, but nonsignificant trend might have been viewed
as evidence consistent with no effect on mortality.
Another trial in acute coronary
syndromes, the Thrombin Receptor Antagonist for Clinical Event
Reduction in Acute Coronary Syndrome (TRACER) trial, evaluated a
thrombin antagonist with a composite outcome of cardiovascular
death, myocardial infraction, stroke, recurrent ischemia with
rehospitalization or urgent coronary revascularization
[86]. The trial of 12,944 patients
randomized 1:1 between the thrombin antagonist and placebo was
terminated for safety reasons with a positive but non-significant
emerging trend in the primary outcome. There were 1,031 primary
events in the treated patients and 1,102 in the placebo controls.
The secondary composite of cardiovascular death, MI and stroke had
822 vs 910 events (P = 0.02). However, the rates of intracranial
bleeding was 1.2% vs 0.2% yielding a hazard ratio of 3.39
(P < 0.001). The data monitoring group decided that the serious
bleeding risks overwhelmed any emerging benefits.
The PROMISE and PROFILE experiences
illustrate the most difficult of the monitoring scenarios, the
emerging negative trend, but they are not unique [87–91]. Trials
with persistent nonsignificant negative trends may have no real
chance of reversing and indicating a benefit from intervention. In
some circumstances, that observation may be sufficient to end the
trial since if a result falls short of establishing benefit, the
intervention would not be used. For example a new expensive or
invasive intervention would likely need to be more effective than a
standard intervention to be used. In other circumstances, a neutral
result may be important, so a small negative trend, still
consistent with a neutral result, would argue for continuation. If
a treatment is already in clinical use on the basis of other
indications, as in the case of the drugs used in PROMISE and
PROFILE, an emerging negative trend may not be sufficient evidence
to alter clinical practice. If a trial terminates early without
resolving convincingly the harmful effects of an intervention, that
intervention may still continue to be used. This practice would put
future patients at risk, and perhaps even participants in the trial
as they return to their usual healthcare system. In that case, the
investment of participants, investigators, and sponsors would not
have resolved an important question. There is a serious and
delicate balance between the responsibility to safeguard the
participants in the trial and the responsibility for all concurrent
and future patients [87].
Trials may continue to their scheduled
termination even though interim results are very positive and
persuasive [92] or the
intervention and control data are so similar that almost surely no
significant results will emerge [93–96]. In one
study of antihypertensive therapy, early significant results did
not override the need for getting long-term experience with an
intensive intervention strategy [92]. Another trial [95] implemented approaches to reduce cigarette
smoking, change diet to lower cholesterol, and used
antihypertensive medications to lower blood pressure in order to
reduce the risk of heart disease. Although early results showed no
trends, it was also not clear how long intervention needed to be
continued before the applied risk factor modifications would take
full effect. It was argued that late favorable results could still
emerge. In fact, they did, though not until some years after the
trial had ended [96]. In a trial
that compared medical and surgical treatment of coronary artery
atherosclerosis, the medical care group had such a favorable
survival experience that there was little room for improvement by
immediate coronary artery bypass graft intervention [94].
The Women’s Health Initiative (WHI)
was one of the largest and most complex trials ever conducted,
certainly in women [97,
98]. This partial factorial trial
evaluated three interventions in postmenopausal women: (1) hormone
replacement therapy (HRT), (2) a low fat diet, and (3) calcium and
vitamin D supplementation. Each intervention, in principle, could
affect multiple organ systems, each with multiple outcomes. For
example, HRT was being evaluated for its effect on cardiovascular
events such as mortality and fatal and non-fatal myocardial
infarction. HRT can also affect bone density, the risk of fracture,
and breast cancer. The HRT component was also stratified into those
with an intact uterus, who received both estrogen and progestin,
and those without a uterus who received estrogen alone. The
estrogen–progestin arm was terminated early due to increases in
deep vein thrombosis, pulmonary embolism, stroke, and breast cancer
and a trend toward increased heart disease as shown in
Fig. 16.6
although there was a benefit in bone fracture as expected
[98]. There was no observed
difference in total mortality or the overall global index, the
composite outcome defined in the protocol, as shown in
Fig. 16.7. The WHI is an excellent example of the
challenges of monitoring trials with composite outcomes where
component trends are not consistent. In such cases, the most
important or most clinically relevant component may have to
dominate in the decision process, even if not completely specified
in the protocol or the monitoring committee charter. Later, the WHI
estrogen-alone arm was also terminated, primarily due to increased
pulmonary embolus and stroke, though there was no difference in
myocardial infarction or total mortality [97]. The formal monitoring process had to
account for multiple interventions, multiple outcomes and repeated
testing.
Fig.
16.6
WHI Kaplan-Meier estimates of cumulative
hazards for selected clinical outcomes [94]. HR
hazard ratio, nCI nominal
confidence interval, aCI
adjusted confidence interval
Fig.
16.7
WHI Kaplan-Meier estimates of cumulative
hazards for global index and death [94]. HR
hazard ratio, nCI nominal
confidence interval, aCI
adjusted confidence interval
A heart failure trial evaluating the
drug tezosentan used a stopping criterion that included futility
[99]. That is, when there was less
than a 10% chance of having a positive beneficial result, the
monitoring committee was to alert the investigators and sponsors
and recommend termination. In fact, at about two-thirds of the way
into the trial, a slightly negative trend was sufficient to make
any chance of a beneficial result unlikely and the trial was
terminated.
In some instances, a trial may be
terminated because the hypothesis being tested has been
convincingly answered by other ongoing trials. This was the case
with trials evaluating warfarin in the treatment of atrial
fibrillation [100]. Between 1985
and 1987, five trials were launched to evaluate warfarin to prevent
strokes in participants with atrial fibrillation. Three of the
trials were terminated early by 1990, reporting significant
reductions in embolic complications. One of the remaining trials
was also terminated early, largely due to the ethical aspects of
continuing trials when the clinical question being tested has
already been answered. The window of opportunity to further
evaluate the intervention had closed.
The Justification for the Use of
Statin in Prevention: An Intervention Trial Evaluating Rosuvastatin
(JUPITER) trial compared a statin agent, which lowers both LDL
cholesterol and C-reactive protein, in 17,802 patients with
elevated high-sensitivity C-reactive protein levels but without
hyperlipidemia [101]. The primary
outcome was the occurrence of the combination of myocardial
infarction, stroke, arterial revascularization, hospitalization for
unstable angina, or death from cardiovascular causes. The trial
demonstrated a clear statin effect of lowering LDL even further as
well as lowering C-reactive protein levels and demonstrated a
corresponding lowering of the primary outcome (hazard ratio (HR) of
.56, p < 0.00001). Similar reductions were observed for
myocardial infarction (HR, 0.46), for stroke (HR, 0.52), for
revascularization or unstable angina (HR, 0.53), for the combined
end point of myocardial infarction, stroke, or death from
cardiovascular causes (HR, 0.53), and for death from any cause (HR,
0.80), all being statistically significant. In addition, all of the
major predefined subgroups were consistent. Still, there was
criticism that the cardiovascular mortality was not significant
even though overall mortality was [102, 103].
This raises the difficult question when using combined outcomes as
the primary if each component or at least some components should
also be statistically significant before terminating a trial. In
general, trials are not designed to demonstrate statistically
significant results for any of the components usually due to low
events for each of them. To do so would require trials much larger
than the one designed. If a component of the combined outcome is of
paramount importance, then that outcome should be established as
the primary and the trial designed accordingly as described in
Chaps. 3 and 8. In the case of the JUPITER trial,
the results for the primary outcome and nearly all of its
components as well as overall mortality appear to be compelling for
a trial to be terminated. This is especially the case when total
mortality is significantly reduced in addition to the primary.
Another approach to a focus on a component of the primary outcome
was in the CHARM program, in which three trials that comprised the
overall program each had cardiovascular death and heart failure
hospitalization as its primary outcome, and the overall program was
powered to assess all-cause mortality. The DMC focused on the
effect on mortality in the overall program as the criterion for
early termination [68].
As we have already discussed, the
decision to terminate a trial is complex. It is never based on a
single outcome and may require more than one DMC meeting before a
recommendation to terminate is reached. Timing of the
recommendation can also be questioned by those external to the
trial. In the Investigation of Lipid Level Management to Understand
its Impact in Atherosclerotic Events (ILLUMINATE) trial
[104], a new agent torcetrapib, a
cholesterylester transfer protein inhibitor that increases HDL
cholesterol, was tested to reduce major cardiovascular events.
ILLUMINATE was a randomized, double-blind study involving 15,067
patients at high cardiovascular risk, receiving either torcetrapib
plus atorvastatin (a statin which lowers LDL cholesterol) or
atorvastatin alone. The primary outcome was defined as time to
death from coronary heart disease, nonfatal myocardial infarction,
stroke, or hospitalization for unstable angina, whichever occurred
first. ILLUMINATE clearly demonstrated an increase in HDL, which
would be expected to cause a reduction in cardiovascular risk.
However, the trial was terminated early by the DMC and the
investigators because of an increased risk of death and cardiac
events in patients receiving torcetrapib [104]. To conclude that torcetrapib improved HDL
but caused harmful clinical effects was of course disappointing
since this was the first testing of an exciting new class of drugs.
However, the timing of the recommendation to terminate was
challenged by a regulatory agency, which recognized the complexity
of such decisions but argued that the trial could and perhaps
should have been terminated earlier [105]. Determining at what point there is
sufficient and compelling evidence to make a recommendation for
termination is often challenging. DMCs do not have the benefit of
hindsight while in process of monitoring a trial.
On occasion, trials may have achieved
a significant benefit, or show strong trends for benefit, but the
DMC recommend early termination for safety reasons. Two trials, the
Thrombin Receptor Antagonist in Secondary Prevention of
Atherothrombotic Ischemic Events (TRA 2P) trial [106] and TRACER [86] provide examples of such instances. Both
trials evaluated a new platelet inhibition agent vorapaxar compared
with placebo. TRA 2P had the primary outcome as a composite of
death from cardiovascular causes, myocardial infarction, or stroke.
TRACER had a composite outcome of death from cardiovascular causes,
myocardial infarction, stroke, recurrent ischemia with
rehospitalization, or urgent coronary revascularization. Both
trials, TRA 2P with 26,449 patients and TRACER with 12,944
patients, had statistically significant beneficial effects in their
respective primary outcomes (HR of 0.87 and 0.89). However, the
DMCs for both trials recommended early termination and/or
modification of the protocol for unacceptable bleeding
complications including intracranial hemorrhage.
In all of these studies, the decisions
were difficult and involved many analyses, thorough review of the
literature, and an understanding of the biological processes. As
described above, a number of questions must be answered before
serious consideration should be given to early termination. As
noted elsewhere, the relationship between clinical trials and
practice is very complex and this complexity is evident in the
monitoring process [107,
108].
Decision to Extend a Trial
The question of whether to extend a
trial beyond its original sample size or planned period of
follow-up may arise. Suppose the mortality rate over a 2-year
period in the control group is assumed to be 40%. (This estimate
may be based on data from another trial involving a similar
population.) Also specified is that the sample size should be large
enough to detect a 25% reduction due to the intervention, with a
two-sided significance level of 5% and a power of 90%. The total
sample size is, therefore, approximately 960. However, say that
early in the study, the mortality rate in the control group appears
somewhat lower than anticipated, closer to 30%. This difference may
result from a change in the study population, selection factors in
the trial, or new concomitant therapies. If no design changes are
made, the intervention would have to be more effective (30%
reduction rather than 25%) for the difference between groups to be
detected with the same power. Alternatively, the investigators
would have to be satisfied with approximately 75% power of
detecting the originally anticipated 25% reduction in mortality. If
it is unreasonable to expect a 30% benefit and if a 75% power is
unacceptable, the design needs modification. Modifying the design
to increase sample size or extend follow-up can inflate type 1
error if it is done with knowledge of the observed intervention
effect and not pre-specified. Even when the process is
pre-specified, because they may be aware of other data suggesting
reasons not to extend the trial, the DMC is usually not involved in
such decisions. Changes may be made by a third party either
according to a pre-specified plan, or with access to certain
summaries of follow-up data, but not to estimates of the
intervention effect.
In the above example, given the lower
control group mortality rate, approximately 1,450 participants
would be required to detect a 25% reduction in mortality, while
maintaining a power of 90%. Another option is to extend the length
of follow-up, which would increase the total number of events. A
combination of these two approaches can also be tried (e.g.
[109]). Another approach that has
been used [35, 36] is to fix the target of the trial to be a
specified number of primary events in the control group or the
overall number. This is often referred to as “event driven” trials.
If event rates are low, it may take longer follow-up per
participant or more randomized participants, or both, to reach the
required number of events. In any case, the target is the number of
events. In the above situations, only data from the control group
or the combined groups are used. No knowledge of what is happening
in the intervention group is needed. In our example, if the event
rate is closer to 30% than the assumed 40%, then the expected
number of events under the null hypothesis, 390, would not be
achieved. The trial could achieve the prespecified target number of
events by increasing recruitment, increasing the length of
follow-up or a combination.
The concept of adaptive designs has
already been discussed in Chap. 5. Adaptive designs can be used in
trials with overall lower event rates or increased variability, or
when emerging trends are smaller than planned for but yet of
clinical interest. Modifying the design once the trial is underway
due to lower event rates or increased variability is rather
straightforward. In a trial of antenatal steroid administration
[110], the incidence of infant
respiratory distress in the control group was much less than
anticipated. Early in the study, the investigators decided to
increase the sample size by extending the recruitment phase. In
another trial, the protocol specifically called for increasing the
sample size if the control group event rate was less than assumed
[111]. As described in the sample
size chapter, power is the probability of detecting a treatment
effect if there truly is an effect. This probability is computed at
the beginning of the trial during the design phase. The design goal
is to set this probability at a range from 0.80 to 0.95 with an
appropriate sample size. Sometimes this probability, or power, is
referred to as “unconditional power” to distinguish it from
“conditional power” to be described in more detail in the next
chapter. Adjustments to sample size based on overall event rates or
variability estimates can preserve the power (or unconditional
power). No account of emerging trends is used in this
recalculation.
The issue of whether the control group
event rate or the overall event rate should be used in this sample
size reassessment must be considered. It might seem intuitive that
the emerging control group event rate should be used since it was
the estimated control group rate that was initially used in the
sample size calculation, as described in Chap. 8. However, to reveal the control
group rate to the investigators may unblind the emerging trend if
they are also aware of the overall number of events. The use of the
overall event rate would avoid this potential problem.
Additionally, there are statistical arguments that under the null
hypothesis, the overall rate is the more appropriate one to use
because it is likely to be more stable, particularly if the sample
size re-estimation is done early in the trial. Many prefer to use
the overall event rate, but in either case, this must be decided
while the protocol and data monitoring procedures are being
developed.
However, modifying the design based on
emerging trends is more complicated (see Chap. 5) and will be discussed in more
technical detail in the next chapter. Despite the statistical
literature for different approaches [112–115] and
some criticism [116,
117], only a few applications of
this type of adaptive design have been utilized. One such trial is
the African-American Heart Failure Trial (A-HeFT) [118], a trial in African Americans with
advanced heart failure using a combination of two established
drugs. The primary outcome consisted of a weighted score of death,
hospitalization, and quality of life. Mortality was among the
secondary outcomes. The trial utilized an adaptive design
[113] that required the
monitoring committee to assess variability of this novel primary
outcome and the emerging trend to make sample size adjustment
recommendations to the trial leaders. The reason for the adaptive
design was that little previous data were available for this
combined outcome so estimates of variability were not adequate to
compute a reliable sample size. Little experience with the outcome
also limited the assessment of potential drug effect on this
outcome. A group sequential boundary was established using a
Lan–DeMets alpha spending function of the O’Brien–Fleming type (see
Chapter 17) for monitoring benefit or harm
for the composite outcome, as described in the next chapter. This
adaptive procedure was followed as planned and the sample size was
increased from 800 to 1,100. Meanwhile, the monitoring committee
was observing a mortality trend favoring the combination drug but
there was no sequential monitoring plan prespecified for this
outcome. The monitoring committee elected to utilize the same
sequential boundary specified for the primary composite outcome to
monitor mortality. Although not ideal while the trial was ongoing,
it was done before the mortality difference became nominally
significant. At the last scheduled meeting of the monitoring
committee, the difference was nominally significant at the 0.05
level but had not crossed the sequential boundary. The committee
decided to conduct an additional review of the data. At that
additional review, the mortality difference was nominally
significant (p = 0.01) and
had, in fact, crossed the sequential O’Brien–Fleming boundary. The
committee recommended early termination both because of a
significant mortality benefit and a primary outcome that was
nominally significant, along with a consistency across the
components of the composite outcome and relevant subgroups.
While the statistical methods for
adaptive designs based on emerging trends to reset the sample size
exist, the use of these methods is still evolving. A more technical
discussion of specific trend adaptive designs is provided in the
next chapter. One concern is whether the application of the
pre-specified algorithm, according to the statistical plan, may
reveal information about the size and direction of the emerging
trend to those blind to the data. These algorithms can be “reverse
engineered” to obtain a reasonable estimate of the emerging trend.
We know of no example to date where this revelation has caused a
problem but in principle this could create bias in participant
selection or recruitment efforts or even participant assessment.
Thus, mechanisms for implementation of trend adaptive trials are
needed that protect the integrity of the trial.
If only the control group event rate
and not the intervention effect is used in the recalculation of
sample size, then an increase could be recommended when the
observed difference between the intervention and control groups is
actually larger than originally expected. Thus, in the hypothetical
example described above, if early data really did show a 30%
benefit from intervention, an increased sample size might not be
needed to maintain the desired power of 90%. For this reason,
despite the shortcomings of existing adaptive designs, one would
not like to make a recommendation about extension without also
considering the observed effect of intervention. Computing
conditional power is one way of incorporating these results, and
some methods in the adaptive design literature have formalized such
as approach [112]. Conditional
power is the probability that the test statistic will be larger
than the critical value, given that a portion of the statistic is
already known from the observed data and described in the next
chapter. As in other power calculations, the assumed true
difference in response variables between groups must be specified.
When the early intervention experience is better than expected, the
conditional power will be large. When the intervention is doing
worse than anticipated, the conditional power will be small. The
conditional power concept utilizes knowledge of outcome in both the
intervention and control groups and is, therefore, controversial.
Nevertheless, the concept attempts to quantify the decision to
extend.
Whatever adjustments are made to
either sample size or the length of follow-up, they should be made
as early in the trial as possible or as part of a planned adaptive
design strategy. Early adjustments should diminish the criticism
that the trial leadership waited until the last minute to see
whether the results would achieve some prespecified significance
level before changing the study design. The technical details for
the statistical methods to adjust sample size based on interim
results are covered in the next chapter.
As mentioned earlier, one challenge in
adaptive designs using interim effects that remains unresolved is
who should make the calculations and perhaps recommend a sample
size increase. The monitoring committee is of course aware of the
interim results for the primary outcome but also for the other
secondary outcomes and adverse event outcomes as well as overall
conduct. The sample size calculations based on the primary events
and emerging trends may recommend an increase in sample size but
the overall profile of the intervention effects may not support
such an increase. Knowing all of the interim results may place the
DMC in an awkward and even ethical dilemma.
Traditionally, DMCs have not been
directly involved in the trial design except to possible terminate
a trial early. Based on our experience to date, we do not recommend
that the monitoring committee engage in the adaptive design if
based on emerging trends.
Accelerated Approval Paradigm
One special case of extending a trial
is presented in the accelerated approval paradigm as illustrated by
the recent FDA guidelines for new interventions for diabetes
[119]. Diabetes is a serious
disease with fatal and nonfatal consequences. Thus, getting new
interventions into clinical practice is a priority. A typical
regulatory approval historically may have been based on a drug’s
ability to lower glucose or HbA1c, which is believed to reduce the
risk of diabetes. However, trials in diabetes have raised the issue
of whether a new drug might in fact raise cardiovascular (CV) risk.
Thus, these new FDA guidelines propose a two-step process. The
first step is to rule out a substantial increase in relative risk
of 1.8. If and when that criteria is met, the pharmaceutical
sponsor can submit their data to get a conditional FDA regulatory
approval and be able to market their drug on the condition that
they gather additional data to rule out an increase in CV risk of
1.3 or greater. This could be accomplished through two consecutive
trials, one smaller trial with approximately 200 CV events to rule
out a CV risk of 1.8 followed by a second larger trial with
approximately 600 CV events to rule out a CV risk of 1.3.
Alternatively, one large trial could be designed such that when the
95% confidence interval excludes a CV risk of 1.8, the monitoring
committee could alert the sponsor to that fact and the regulatory
submission for drug approval would be initiated. However, the trial
would continue to gather for CV data to rule out a risk of 1.3. A
problem for trial continuation arises however if the new drug is
fact given regulatory conditional approval. At that point, the
clinical and private community is now aware of the “interim”
results submitted to rule out the CV risk of 1.8, with pressure to
share some degree of detail about the results. Whether diabetes
patients will continue adhere to their assigned, presumably
blinded, trial medication or even agree to be entered if not
already randomized is a serious question. Failure to adhere to the
assigned therapy will bias the risk assessment towards the null and
thus a result favoring a rule out of the 1.3 CV risk.
Employing the two sequential trial
approach also has problems. First, it adds to the length of the
period where a new drug is under development. Second, knowing the
results of the first trial which ruled out a CV risk of 1.8 may
influence the profile of the diabetes patients in the second trial,
either through physician or patient decision not to participate.
For example, more serious risk patients may choose not to be
randomized and thus lowering the overall CV risk.
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