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.
The authors did not receive grants or outside funding in support of their research for or preparation of this manuscript. They did not receive payments or other benefits or a commitment or agreement to provide such benefits from a commercial entity. No commercial entity paid or directed, or agreed to pay or direct, any benefits to any research fund, foundation, educational institution, or other charitable or nonprofit organization with which the authors are affiliated or associated.
1. Montori VM, Guyatt GH. Intention-to-treat principle. CMAJ. 2001;165: 1339-41.
2. Heritier SR, Gebski VJ, Keech AC. Inclusion of patients in clinical trial analysis: the intention-to-treat principle. Med J Aust. 2003;179: 438-40.
3. Wright CC, Sim J. Intention-to-treat approach to data from randomized controlled trials: a sensitivity analysis. J Clin Epidemiol. 2003;56: 833-42.
4. Guyatt GH, Sackett DL, Cook DJ. Users' guides to the medical literature. II. How to use an article about therapy or prevention. A. Are the results of the study valid? Evidence-Based Medicine Working Group. JAMA. 1993;270: 2598-601.
5. Gibaldi M, Sullivan S. Intention-to-treat analysis in randomized trials: who gets counted? J Clin Pharmacol. 1997;37: 667-72.
6. Fergusson D, Aaron SD, Guyatt G, Hebert P. Post-randomisation exclusions: the intention to treat principle and excluding patients from analysis. BMJ. 2002;325: 652-4.
7. Begg CB. Ruminations on the intent-to-treat principle. Control Clin Trials. 2000;21: 241-3.