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Table 4.3 Categories of outcome measures, according to the level of evidence for efcacy
Categories of outcome measures
Level of evidence for efcacy Example
Level 1 True efcacy measure Death or hospitalization in
pulmonary arterial hypertension or
heart failure
Level 2 Validated surrogate Six-minute walk distance in
pulmonary arterial hypertension
Level 3 Nonvalidated surrogate “reasonably likely to
predict clinical benet”
Progression-free survival in some
settings of cancer
Level 4 Correlate that measures biological activity but
has not been established to be clinically
meaningful at later stages
Negative blood cultures in treating
various infectious diseases
The advantage of using a surrogate endpoint, especially in early-stage trials, is
that it may allow recruitment of fewer participants because of a stronger treatment
effect, less variability, and higher response rate, thus making it easier to detect a true
treatment effect in a small trial of short duration. The value, however, is highly
dependent upon how strongly the surrogate predicts a more clinically meaningful
outcome in later-stage trials. For a validated surrogate, the strength is so high that
regulators will accept the endpoint as the primary basis of approval. One example is
the use of blood pressure readings for antihypertensive drugs instead of more clini-
cally meaningful endpoints of cardiovascular morbidity or mortality.
Fleming and Powers (Fleming and Powers 2012) have provided examples of dif-
ferent categories of outcome measures, according to the level of evidence for ef-
cacy. Levels 2, 3, and 4 are considered “indirect” endpoints. Some examples are
included in Table4.3.
Some surrogate endpoints—for example, blood pressure (for hypertension), cho-
lesterol levels (for elevated cholesterol), or 6-minute walk distance (for pulmonary
arterial hypertension)—are highly validated and acceptable endpoints for pivotal
phase 3 drug registration trials with FDA, but others are not considered sufcient to
validate efcacy and safety because they measure only a small aspect of a complex
human disease. Although FDA favors hard clinical endpoints, the use of a nonvali-
dated surrogate endpoint can still be useful in early-stage trials to complement other
endpoints if it may predict clinical outcomes.
Finally, when considering endpoints, it can be challenging to determine what a
clinically meaningful effect is. For example, assume there is an ordinal pain scale
measuring 1–10 (with 10 being the highest level of pain). With study treatment, how
would you interpret the meaningfulness of a mean change from baseline to week 8
of 2.8? With pain outcomes, clinicians and regulators agree that a 50% reduction in
pain is a clinically meaningful outcome. As a result, a “responder endpoint” would
be the proportion of patients with a 50% reduction in pain at treatment completion.
Similarly, for drugs intended to treat nicotine dependence, the proportion of partici-
pants who achieve continuous abstinence (conrmed by exhaled carbon monoxide)
during the last 4weeks of treatment is recognized as more clinically meaningful
than mean change from baseline in the number of cigarettes smoked per week.
While differences between active drug and control groups would still need to be
assessed for the minimal clinically important difference, an endpoint where patients
D. Mochly-Rosen et al.
171
are either “responders” or “nonresponders” based on whether they cross predened
thresholds is advantageous when available. Such outcomes build in the concept of
clinical meaningfulness; the proportion of patients who are responders serves as an
easy-to-interpret measurement of the treatment’s effectiveness. In addition, unlike
“change from baseline” endpoints, responder endpoints that involve “proportion of
participants” do not require estimations of variability for sample size calculations.
In small clinical trials, however, responder endpoints should be supplemented by
other endpoints as they use less data than a continuous endpoint and may in some
circumstances require more patients to show the existence of treatment effects.
4.4.9 Importance ofBiostatisticians andClinical Trialists
Just as in preclinical animal studies, it is important to involve a biostatistician and
clinical trialist in discussing both study design and the number of study participants
(sample size) to detect a true treatment effect. A sample size calculation does not
indicate what the result will be, but rather is a prestudy exercise that conveys the
degree of condence that a given number of participants will be adequate to detect
a predetermined treatment effect at a prespecied statistical signicance level. This
adequacy is determined in part by agreeing on what is usually a high probability to
conclude that a treatment has efcacy when it truly does (power), usually 80% or
90%, and a low probability to falsely conclude a treatment has efcacy when it truly
does not (alpha, usually 5% or less). Pilot studies with small numbers of participants
may have lower power than desired (i.e., decreased ability to detect a true treatment
effect) at a standard signicance level.
Sample size calculation relies on subjective choice of four variables:
1. Estimated treatment effect.
2. Number of participants per group.
3. Power is the probability of detecting a given treatment effect or greater, if one
truly exists (“true positive”). Low power can lead to falsely rejecting an effective
therapy (Type II error).
4. Signicance level, or alpha, is the probability of falsely detecting a treatment
effect when none truly exists (“false positive”). This can lead to falsely accepting
an ineffective therapy (Type I error).
Common misconceptions for not conducting sample size calculations:
• “Study is of a pilot nature.”
• “Treatment effect of investigational drug is unknown.”
• “Standard deviation for effect estimation is unknown.”
• “Unable to power study to be statistically signicant.”
• “This is a safety study” (when it isn’t).
Power is exclusively a pretrial concept to estimate the probability of predeter-
mined results or greater under a specied hypothesis. A common error is estimating
4 Preparing fortheClinic
172
a treatment effect that is unrealistically favorable to justify both a small number of
evaluable patients and a desire for 80% power. Another common error is expecting
a biostatistician to determine what the estimated treatment effect is; rather, the clini-
cal investigator or clinician must provide the effect to the biostatistician to help
determine the number of participants needed to detect this effect or greater at a
signicance level. This treatment effect is ideally the “minimal clinically important
difference” (MCID) between active and placebo groups, which is the smallest dif-
ference in an outcome measure that is clinically meaningful. If the study is powered
to detect a highly robust effect, it may not have enough participants to detect a
smaller but clinically relevant effect.
As an example, patients with pulmonary arterial hypertension have impairment
in exercise capacity. How far one can walk in 6min is considered a validated sur-
rogate endpoint for more clinically relevant endpoints, such as time of clinical wors-
ening or hospitalization. An approximately 35-m mean change from baseline to
nal assessment (with a standard deviation of 60m) is considered the minimum
clinically relevant difference; as a result, a change of 10m would not be considered
meaningful and a change of 50m would be viewed as highly robust. Studies using
exercise capacity (6-min walk distance) in pulmonary arterial hypertension are
designed with reasonable power (80–90%) to detect this MCID or greater at a sig-
nicance level if it truly exists. Having too few participants to detect the MCID is
called an “underpowered” study; it does not have the optimal ability to detect, at a
signicance level, a true treatment effect that is clinically meaningful.
Because academic trials are often resource-limited with fewer numbers of par-
ticipants, such trials may not be able to detect a true and clinically relevant treatment
effect with high probability (underpowered). At a given sample size, factors that
contribute to lowered power to detect a given clinically relevant effect include high
placebo response rates, low event rates, modest treatment effects, and benet from
slowing of worsening (as opposed to improvement per se). Despite this concern,
academic studies can have sufcient ability to evaluate for preliminary evidence of
safety, efcacy, and variability, including the presence of a biologic signal.
Box 4.8: Common Pitfalls to Avoid
1. Not appreciating the value of sample size determination.
2. Not incorporating surrogate endpoints, including biomarkers, that may
help determine a biologic effect in an early-stage trial.
3. Starting with too high a dose or escalating the dose too quickly in early
safety studies.
4. Trying to make denitive efcacy conclusions with an underpowered study.
5. Working “backwards” with a given number of study participants in sample
size calculations to have high power to detect an unrealistically high treat-
ment effect.
6. Retroactively looking through subsets of data to try to show efcacy.
7. Trial sites that deviate from the protocol in enrollment criteria, record
keeping, or measurements.
8. Poor patient retention and missed follow-up visits.
D. Mochly-Rosen et al.
173
4.4.10 Phase 2 Studies
The goal of the phase 2 trial(s) is to obtain preliminary but more denitive data than
from phase 1b trials regarding whether the intervention is safe and effective in the
target patient population. This includes studying the conditions (nal dose, route,
and regimen) and the endpoints (primary, secondary, and surrogate) that will be
used in phase 3 conrmatory trials, as well as continuing to build the drug safety
prole.
Because phase 1 trials have established some level of safety and tolerability (and
possible efcacy in a phase 1b trial of a repurposed drug), phase 2 studies will have
larger participant numbers and typically longer duration. Phase 2 trials usually
study a range of doses in parallel. The dose range is highly dependent on the safety
and PK results obtained in phase 1. Often, surrogate endpoints will be used for evi-
dence of efcacy since they typically require both a smaller sample size and a
shorter trial duration than clinical outcomes. A distinction is sometimes drawn
between a phase 2a trial that studies dose and regimen selection to determine the
maximum dose and a phase 2b trial that focuses on measures of efcacy to nd the
minimally effective dose.
As with phase 1b trials, options for control groups in phase 2 trials include:
• No control group (open label=unblinded).
• Placebo group (open label or blinded).
• Active treatment with a specic (usually approved) drug.
• Standard of care (optimal treatment available).
• Standard of care (clinical practice in real-world setting).
• A crossover design, advantageous for rare diseases or where recruitment is
changing, in which each participant serves as their own control by receiving each
treatment (such as placebo followed by active drug) in succession separated by a
brief period without study drug. An advantage of this internal control (i.e., within
each participant) is eliminating individual participant differences from the over-
all treatment effect, thus enhancing statistical power with fewer participants in a
rare condition. However, in a crossover study, it is important that the underlying
disease does not signicantly change over the time studied as part of the natural
history and that the effects of one treatment are gone before the next is applied.
Box 4.9: What Surprised an Academic?
When planning our multicenter phase 2 clinical trial targeting patients with
ST elevation myocardial infarction (STEMI), we asked our investigators and
study coordinators at each participating hospital for a realistic prediction of
how many patients they could enroll per month. Their answer was invariably
four to ve-fold higher than their actual enrollment rate. Overcondent study
staff failed to account for a number of factors that limited patient recruitment,
such as the challenges of enrolling patients in the middle of the night when
study staff were not available, other trials competing for the same patients, the
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174
As previously noted, blinding both the research team and patients to the treat-
ment assignment is very important in clinical trial design: not only to prevent inves-
tigator or study staff (unintentional) bias inuencing data collection, but also to best
measure any placebo effects that participants experience. In rare situations (e.g.,
hemodynamic indices in pulmonary arterial hypertension), there is no placebo
effect. That is, patients receiving placebo historically show no change or worsened
hemodynamic effects as part of the natural history of their disease. In this setting,
even though such patients are enrolled on maximum stable (but suboptimal) back-
ground therapy, removing the placebo group from the study design at this stage can
facilitate enrollment in a rare condition while still allowing benet with active treat-
ment to reect a true improvement. A disadvantage of this approach is that the
placebo- adjusted incidence of adverse events cannot be assessed in the absence of
this control group.
While phase 2 studies can be single blinded (study participant does not know
whether receiving active or control), double blinded (participant and trial staff do
not know), or triple blinded (participant, staff, trial sponsor, and core lab analyzing
specimens do not know), an unblinded Data Safety Monitoring Committee can help
inform investigators how to respond to adverse events that arise during the trial.
The sample size should be determined by the number of participants needed to
adequately “power” the trial to observe a clinically meaningful change at a (statisti-
cal) signicance level for the main endpoint of interest. Excellent sample size cal-
culators are available online (see Sect. 4.4 Resources), but it is strongly advised to
consult an experienced clinical trial biostatistician or clinical trialist. The biostatisti-
cian will ask the clinician: “What is the smallest change in a trial endpoint that you
want to be able to detect that is clinically meaningful?” From this information and
published values of the endpoint in the target population, the biostatistician should
be able to provide the number of participants needed to detect the desired effect.
When estimating the expected value for the primary endpoint in the placebo group
based on historical data, it is important to correct for recent improvements in stan-
dard of care that may not be reected in published data from previous studies.
Multiple surrogate endpoints may be evaluated in phase 2 trials to better charac-
terize the safety, tolerability, and efcacy. Often a surrogate endpoint is chosen as
the primary endpoint in phase 2 (and the trial is “powered” on this endpoint) and the
planned phase 3 clinical endpoint is evaluated as a secondary endpoint (since it is
likely to be “underpowered” with the smaller size of the phase 2 trial). A common
example is the use of hemodynamics as the main endpoint in phase 2 pulmonary
fact that only 25% of STEMI patients would meet the eligibility criteria, etc.
When identifying clinical sites and planning for patient recruitment, it is
essential to be very detailed in determining the realistic rate of patient enroll-
ment. Even then, discount the predicted enrollment rate by 50–75%. An
overly long period of patient recruitment will greatly increase the cost of your
clinical trial, and may even lead to failure of your study if you run out of
resources. —KVG
D. Mochly-Rosen et al.
175
arterial hypertension trials, requiring about 20–25 patients/group to be able to detect
the minimally important clinical difference or greater at a signicance level. A sec-
ondary endpoint might include the more clinically relevant endpoint of exercise
capacity, which in a phase 3 trial requires about 100 patients/group. However,
trends, or in some cases a very robust effect for an underpowered endpoint, can
occur and provide evidence of biological plausibility or a meaningful treatment
effect.
The methods to assess the clinical outcome in phase 3 should be clearly estab-
lished and rehearsed at each trial site during phase 2, so that inconsistencies between
sites are minimized and do not affect data integrity. A successful phase 2 program
will help minimize “surprises” in clinical operations and trial conduct that may
occur during the phase 3 program. Phase 2 studies are where most programs falter;
in an evaluation of 9704 programs across the US and other countries from 2011 to
2020, only 28.9% progressed from phase 2 to phase 3 (Fig.4.4) (Biotechnology
Innovation Organization 2021). Some trials fail because the drug does not work,
others because suboptimal study design and conduct may preclude detection of a
true effect. Perhaps most fail the “wallet” test: The clinical effect is not sufcient to
justify further development.
Recommendations
• As you transition from animal to human studies, be aware of the use of
concomitant medications. These can lead to drug–drug interactions, which
may increase or decrease your therapeutic effect or even have a direct
impact on your chosen endpoints.
• If possible, try to determine the MCID as the estimated treatment effect to
power your study. This way you will be able to detect a true treatment
effect that is clinically meaningful at a signicance level. In some cases,
the number of participants needed to achieve this is not realistic in an aca-
demic or early-stage trial. In those situations, identifying clinically impor-
tant effects at study completion can be helped prior to the study by:
– Incorporating multiple biologically related endpoints.
– Use of biomarkers that are biologically plausible.
– Use of validated or reasonably likely validated surrogate endpoints that
may be highly affected by treatment.
– Using relevant assessments with low placebo response rates.
– Specifying outcomes that occur more frequently.
– Enrolling patients at higher risk.
– Making full use of longitudinal data.
– Prolonging nontreatment follow-up.
• Picking the wrong clinical or surrogate endpoints can obscure a true thera-
peutic effect or drastically increase the time and cost of running a clinical
trial. Consult FDA guidance and past clinical trials in your indication (or a
related indication) to see what metrics others have used.
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4.5 Phase 3 Studies
LynFrumkin and TedMcCluskey
Assuming that the phase 1 and 2 clinical trials provide reasonable evidence of safety
and efcacy based on surrogate or more clinically meaningful endpoints, it is time
to request an end-of-phase 2 meeting with FDA.FDA guidance will be critically
important, not only for nalizing plans for the pivotal phase 3 trial(s), but also to
ensure that the sponsor addresses any nonclinical concerns that must be included in
the NDA.
Before registering a new drug, FDA requires two large and robust phase 3 trials
to show safety and efcacy via an approved clinical endpoint with high statistical
condence. In rare cases, after discussion with FDA, highly robust treatments for
serious medical conditions with great unmet needs are approved after a single phase
3 trial with more stringent safety and efcacy requirements.
4.5.1 Trial Design Trends forSmall Clinical Trials
Drug development is difcult. From 2011 to 2020, only around 9% of compounds
(either drugs or biologics) entering phase 1 clinical trials from FDA registration-
enabling development programs successfully progressed through all clinical trial
Resources
• CRAB.Statistical Tools: https://stattools.crab.org/.
• SPARK at Stanford Resources: https://sparkmed.stanford.edu/spark-
scholars/resources/#research- resources.
Fig. 4.4 Overall phase transition success rates from phase 1 to NDA/BLA for 9704 international
programs from 2011 to 2020, adapted from Biomedtracker
®
and Pharmapremia
®
, 2020
(Biotechnology Innovation Organization 2021). Abbreviations: BLA Biologics License Application,
NDA New Drug Application; Ph Phase
D. Mochly-Rosen et al.
177
phases to submit a successful application to be registered as a new drug or biologic
(Biotechnology Innovation Organization 2021). This represents a huge nancial
loss in research and development expenses. New trial strategies are emerging to
improve measurements of efcacy and to “fail fast,” that is, rapidly reach go/no-go
evaluation points for safety and efcacy. This also includes novel considerations for
small clinical trials that are unable to recruit large numbers of participants. The US
National Academy of Medicine has emphasized the importance of balancing the
need for clinical trials that are adequately powered for scientic and ethical validity
with the reality that, in certain situations (rare diseases, unique study populations
such as astronauts, or emergency situations), the number of potential study partici-
pants may be quite limited. Such challenges can affect study interpretation (Evans
Jr and Ilstad 2001).
Small clinical trials, whether due to a low disease prevalence or limited resources,
may be able to detect only gross effects and run the risk of not identifying true effec-
tiveness and adverse events. Approaches, such as full use of longitudinal data, non-
treatment follow-up, including multiple endpoints (appreciating that many
comparisons increase the likelihood that a chance association could be deemed
causal), and use of composite endpoints (combining several outcomes into a single
outcome measure), may improve the ability to detect a true treatment effect in a
small clinical trial (Day etal. 2018).
Besides the crossover design previously mentioned, there are other designs to
optimize sample size. An adaptive trial design allows changes to a trial after its
initiation without affecting data validity or integrity (Bhatt and Mehta 2016).
Adaptive designs can be applied to all trial phases, from early-phase dose escalation
to late-stage conrmatory trials. For example, in one adaptive trial design, blinded
trial data by masked treatment assignment can be periodically evaluated for safety
and efcacy metrics while the trial is ongoing to determine whether a sample size
re-adjustment is necessary. Besides adjustments to enrollment size, premature clo-
sure of the trial for early “success” or “failure” can also be determined in some cases.
Whereas placebo is traditionally the most common type of control for a clinical
trial, the use of active controls is growing and will likely increase more in the future.
In clinical trials, regulations require new agents to beat placebo, not approved drugs.
However, in indications where there is an approved drug on the market, head-to-
head comparison with the investigational drug in a trial that requires more partici-
pants to be adequately powered can allow a direct comparison of therapeutic
benets. This benets patients and physicians by evaluating whether a newly
approved drug provides a benet over older (possibly generic) drugs. Companies
were previously reticent to run active control trials for fear their investigational drug
would not be more effective than previously approved drugs. Recent legislation in
the US aimed at “comparative effectiveness” will likely increase the use of active
controls.
Enrollment strategies are also important. A sponsor can be a “lumper” with broad
inclusion criteria for enrollment or a “splitter” that narrowly denes participant
enrollment. Lumpers are often focused on maximizing potential market size after
drug approval or speeding enrollment rates. Splitters, on the other hand, are worried
4 Preparing fortheClinic
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about variation within the target indication and select for those patients most likely
to benet from the investigational drug. This latter approach is critically important
in some conditions (e.g., pulmonary arterial hypertension) where certain subtypes
(idiopathic, heritable, connective tissue disease, and congenital heart disease) may
respond to various treatments better than other subtypes. In this case, enrolling
those most likely to respond in a clinical trial can better detect a true treatment effect
that might be missed by enrolling both historical “good responders” and those who
poorly respond. With the demonstration of safety and efcacy in the former group,
the latter group can subsequently be evaluated in separate trials. Both enrollment
strategies have pros and cons; specic indications may favor one strategy over
the other.
4.5.2 Final Points
Creating the proper database to collect study information and formulate plans for
data analyses, data monitoring, and review of adverse events is critical to address
before study start. Regardless of whether a clinical trial is investigator-, govern-
ment-, or company-sponsored, it must be conducted under a protocol; the ethical
principles stated in the 2013 version of the Declaration of Helsinki; applicable
guidelines on Good Clinical Practice; and all applicable federal, state, and local
laws, rules, and regulations (U.S.Food and Drug Administration 2018) to maximize
clinical trial quality and participant safety. In addition, several important “internal”
nancial and operational issues must be addressed when transitioning into clinical
studies. Trial costs must be estimated, and internal budget and personnel resources
must be planned and accounted for to complete the initial study, including nontreat-
ment follow-up. Considerations for patient enrollment rates at each clinical site can
help predict the time required to complete the clinical trial. Insurance, IRB fees, and
funds for investigator training and auditing must also be in place.
The Bottom Line
The successful execution of a clinical trial plan requires a team effort and
detailed planning. Since it is the most expensive part of drug development,
setbacks in execution of clinical trials (e.g., too slow enrollment, shortage of
drug, delay in drug arrival to the clinical sites, inappropriate blinding, improp-
erly designed trial, inadequate sample size) can “sink” the program for bud-
getary reasons, poor enrollment, or a “negative” result from the inability to
detect a true treatment effect rather than because the drug is not effective.
D. Mochly-Rosen et al.
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Key Terms andAbbreviations
Key Terms
Active Pharmaceutical Ingredient (API): The pharmacologically active
molecule.
Biologics License Application (BLA): Request for permission to introduce a
biologic product into interstate commerce in the US.
Biosimilar: Generic version of a previously approved biologic therapeutic.
Chemistry, Manufacturing, and Controls (CMC): Manufacturing proce-
dures and specications that must be followed to ensure product safety and
consistency between batches.
Clinical Endpoint: A measure of something a patient would experience or
report.
Common Technical Document (CTD): Standardized ve-module format for
submission of regulatory applications to CDER and CBER.
Contract Development and Manufacturing Organization (CDMO): An
external company that does both formulation development and manufac-
turing of a drug product.
Contract Manufacturing Organization (CMO): An external company that
manufactures a preformulated drug.
Double-Blinded: Neither the participants nor study staff knows which treat-
ment the participant is assigned to.
Drug Product (DP): Encompasses API and inactive components such as
binders, capsule, etc., that composes the nal drug formulation of the phar-
macologically active molecule administered to patients.
Drug Substance (DS): The pharmacologically active biological material—
same as API and used interchangeably.
FDA Center for Biologics Evaluation and Research (CBER): Responsible
for regulation of biological and related products such as blood, vaccines,
and cellular and gene therapies.
FDA Center for Devices and Radiological Health (CDRH): Responsible
for ensuring the safety and effectiveness of medical devices and the safety
of radiation-emitting products.
FDA Center for Drug Evaluation and Research (CDER): Responsible for
regulating the safe and effective use of over-the-counter and prescription
drugs, including monoclonal antibodies, immunomodulators, growth fac-
tors, and other proteintherapeutics.
First in Human (FIH): A clinical trial in which a treatment is tested in
humans for the rst time.
Good Manufacturing Practice (GMP): Exacting procedures and documen-
tation of quality assurance carried out at a certied facility (sometimes
referred to as “cGMP” for “current” practice).
4 Preparing fortheClinic