Extract
Randomization in clinical trials reduces bias. Its intent is to generate
groups of patients that are comparable with each other before starting a
study. As a result, both known and unknown patient factors that may affect the
outcome under investigation are balanced between the treatment groups,
minimizing the risk of differences between the two groups at the onset of the
trial. This helps to ensure that differences in outcomes observed between the
groups are the result of the intervention. Anything that compromises the
balance of these factors may introduce bias into the
results1,2.
If an imbalance between the groups skews the results in favor of one
intervention over the other, this can lead to a biased study. Therefore, a
randomized, double-blinded, placebo-controlled (when appropriate) trial with
intention-to-treat analysis is considered to be the highest level of evidence
in clinical research. This provides the clearest insight into the effect of
the intervention being studied by controlling for as many factors as
possible.
Randomization in clinical trials reduces bias. Its intent is to generate
groups of patients that are comparable with each other before starting a
study. As a result, both known and unknown patient factors that may affect the
outcome under investigation are balanced between the treatment groups,
minimizing the risk of differences between the two groups at the onset of the
trial. This helps to ensure that differences in outcomes observed between the
groups are the result of the intervention. Anything that compromises the
balance of these factors may introduce bias into the
results1,2.
If an imbalance between the groups skews the results in favor of one
intervention over the other, this can lead to a biased study. Therefore, a
randomized, double-blinded, placebo-controlled (when appropriate) trial with
intention-to-treat analysis is considered to be the highest level of evidence
in clinical research. This provides the clearest insight into the effect of
the intervention being studied by controlling for as many factors as
possible.
Intention-to-treat analysis compares study groups in terms of the treatment
to which they were randomly allocated, irrespective of the treatment they
actually
received2-4.
If subjects do not receive the treatment to which they were originally
randomized, they are in violation of the study protocol. There are several
examples of protocol violation, including crossover from one treatment group
to another, patients lost to follow-up, and inclusion of patients who should
not have been included. Regardless of protocol violation, intention-to-treat
analysis is done according to the originally assigned treatment groups because
this helps to preserve the value of randomization.
Some investigators exclude from analysis any participants who violate the
study protocol (e.g., those who cross over, are lost to follow-up, or have
insufficient follow-up). This is known as per-protocol
analysis2. Patients
who deviate from the protocol are eliminated, and there is no guarantee that
the residual groups are
comparable5. The
remaining treatment groups may be unbalanced in their initial patient factors.
This undermines the reason for randomization and may introduce
bias5. By excluding
nonadherent participants from the analysis, those who may be destined to have
a better outcome are left
behind1. This may
overstate treatment efficacy. As such, perprotocol analysis should be
considered a "best-case scenario."
Let us illustrate these principles with a hypothetical example. Imagine a
randomized trial in which treatment with a cast is compared with
intramedullary nailing for low-energy fractures of the tibia. Assume that both
treatments are equivalent. Fifty patients are enrolled, with twenty-five
randomized to each arm of the study (Fig.
1). The primary end point of the trial is the number of patients
returning to a preinjury level of function. Ten of the fifty patients are
unmotivated and are destined for a poor outcome regardless of treatment
assignment. In real life, patient motivation is not easily measurable, but
randomization equally distributes immeasurable patient factors just as it does
measurable traits. In our example, randomization equally distributes the
unmotivated patients between the two groups (five in each treatment arm). All
of the patients in the intramedullary nail group have uneventful surgery. All
twenty-five patients in the other group have a cast applied, but five return
for the one-week follow-up visit and want intramedullary nailing. Three of
these five patients are unmotivated. At the end of the trial, all of the
unmotivated patients have functional limitations regardless of the treatment
they received.
With use of the per-protocol method of analysis, the five patients who
cross over are excluded from analysis. The remaining groups are now no longer
balanced, with more unmotivated patients in the intramedullary nail group.
This leaves twenty patients in the cast group and the original twenty-five
patients in the intramedullary nail group for consideration. Two (10%) of the
twenty patients in the cast group and five (20%) of the twenty-five patients
in the intramedullary nail group are unmotivated and have functional
limitations. Therefore, it appears as if cast treatment is superior. In
reality, the unmotivated patients will all do poorly regardless of the
treatment they
receive4. The
perprotocol method systematically excludes the unmotivated patients from the
cast group and introduces bias. With the application of the intention-to-treat
principle, the patients who cross over are analyzed in the group to which they
were originally randomized. As such, the number of patients who have
limitations are equal (20%) in the two groups (five of twenty-five in each
group). This is what we expect as we know that unmotivated patients do poorly
despite treatment with a cast or an intramedullary nail.
Some investigators analyze patients according to the treatment they
actually received rather than exclude them as in a per-protocol analysis. This
is known as treatment-received
analysis2. Let us
consider what happens if the five patients who cross over from cast treatment
to intramedullary nailing are analyzed as patients in the intramedullary nail
group (Fig. 2). Two (10%) of
twenty patients in the cast group and eight (27%) of thirty patients in the
intramedullary nail group are unmotivated and do poorly. This worsens the
bias, and it now appears as if cast treatment is far superior. An
intention-to-treat analysis again solves this problem.
A patient can initiate crossover in treatment as the previous example
illustrates. What happens when a surgeon needs to change a patient's
randomized treatment? Consider a randomized trial of reamed compared with
unreamed nailing for diaphyseal fractures of the tibia. A patient randomized
to unreamed nailing has a canal that is too narrow for the smallest nail. This
is discovered intraoperatively as the surgeon attempts to pass the nail. In
this situation, the patient was prematurely randomized into the
trial6. Ideally, it
should have been identified that the patient was not a candidate for unreamed
nailing and should never have been included in the study. In other words, a
patient must be equally eligible for both interventions to be randomized. This
patient never received the randomized intervention (i.e., unreamed nailing)
and thus was inappropriately included initially and can be excluded from the
analysis of
data6.
Intention-to-treat analysis provides a conservative estimate of treatment
effect, as this effect is diluted because of
noncompliance5. It
may, however, underestimate the magnitude of treatment effect in compliant
patients when noncompliance is
considerable1. For
example, imagine a pill that completely prevents deep vein thrombosis after
total hip arthroplasty. Only 50% of patients are compliant with treatment, and
none have deep vein thrombosis develop. The other 50% are noncompliant, and
half of them have deep vein thrombosis develop. With an intention-to-treat
analysis, it appears as if the medication is 75% effective (50% + 25%). In
reality, the pill is 100% effective and the treatment effect is grossly
underestimated because of noncompliance.
The best way to deal with noncompliance is to design a study to minimize
it. An intention-to-treat analysis attempts to correct statistically for
protocol violation, but it does not redeem problems with study
design3,7.
Therefore, randomization should be done as close as possible in time to the
intervention to minimize crossover, study participants should be blinded to
the treatment they will receive, and surgeons should be sufficiently skilled
to perform either of the treatments the patient may be randomized to receive.
By maximizing compliance with the original randomization assignments, bias in
the analysis of the results is minimized. In addition, the method of
randomization should be truly random. For example, subjects should be
randomized to treatment group by sequential envelope or random-number
assignment rather than by subject surname or day of the week.
As can be seen, an intention-to-treat approach is not a remedy for unsound
design or incomplete follow-up. In fact, substantial loss to follow-up alters
the initial randomization and introduces exactly the same bias as a
perprotocol
analysis1. One
cannot assume that all patients who are lost to follow-up do well. A
conservative approach is to assume that all patients who are lost to follow-up
do poorly. The truth is somewhere between "all patients do well"
and "all patients do poorly." This is known as a sensitivity
analysis. An acceptable number of patients lost to follow-up depends on the
individual study. The more subjects who are lost to follow-up, the greater the
chance that the results are
biased4. If a
sensitivity analysis was not performed in a trial, clinicians can decide for
themselves if the number of subjects lost to follow-up is excessive. This can
be done by recalculating the results with use of the assumption that all of
the missing subjects did poorly or did well. If the results are not changed
with these calculations, then the number of subjects lost to follow-up was not
excessive4.
There are other approaches to deal with missing data, but all are imperfect
and a full discussion of this problem is beyond the scope of this article. In
summary, the results from studies with substantial loss to follow-up are
weaker, and an intention-to-treat analysis cannot eliminate bias in this
situation7.
In conclusion, intention-to-treat analysis compares study groups in terms
of the treatment to which they were randomly allocated, regardless of the
treatment they actually received. This preserves randomization and minimizes
bias. Intention-to-treat analysis provides a conservative estimate of
treatment effect; however, the underestimation can be substantial when
noncompliance is high. As such, noncompliance should be kept to a minimum
through the study design, as intention-to-treat analysis "cannot redeem
poor quality data resulting from inadequate design or implementation of a
study."3
Nonetheless, intention-to-treat analysis has an important role to play in the
analysis of data from randomized clinical trials as it minimizes bias and
provides a better estimate of the true treatment effect.
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