Chapter 16
Intention-to-Treat Analysis
16.1 Introduction
A clinical trial of a new therapy (agent, intervention, diagnostic procedure, etc.) has many objectives. One objective is to evaluate whether the therapy has the intended biological or physiological effect, which is often termed pharmacological efficacy in relation to a new pharmaceutical agent. Another is to evaluate the pragmatic use of the therapy in clinical practice, which is often termed simply effectiveness. The intention-to-treat principle refers to a strategy for the design, conduct, and analysis of a clinical trial aimed at assessing the latter, which is the pragmatic effectiveness of a therapy in clinical practice.
An analysis for the assessment of pharmacological efficacy generally excludes subjects who either did not comply with the assigned therapy or could not tolerate it because of adverse effects. Such analyses are often termed per-protocol, efficacy subset, or evaluable subset analyses and involve post hoc subset selection or post hoc exclusions of randomized subjects. Conversely, for the assessment of effectiveness in an intent-to-treat analysis, follow-up data for all randomized subjects should be obtained and included in the analysis. This design is the essence of the intention-to-treat principle.
16.2 Missing Information
16.2.1 Background
The intention-to-treat principle evolved from the evaluation by regulatory officials at the Food and Drug Administration (FDA) [1], as well as scientists from the National Institutes of Health [2] and academia [3], of clinical trials in which post hoc subset selection criteria were applied [4]. In some cases, the data are collected but are excluded at the time of analysis. More often, the protocol allows subjects to terminate follow-up, and thus allows subject data to be excluded (not collected), such that it is only possible to perform an analysis using a post-hoc selected subset. The essential concern with such subset selection, or equivalently post-hoc exclusions, is that the resulting subset may be susceptible to various forms of bias [3,5–7]. A review is provided in Reference 8.
Many who champion the efficacy subset analysis approach argue that statistical techniques may be applied to provide an unbiased analysis under certain assumptions [9]. The essential statistical issue is the extent to which it can be assumed that missing data and omitted data do not introduce a bias under the missing information principle [10] (i.e., that missing/omitted data are ignorable).
16.2.2 Ignorable Missing Data
Missing data refers to data that are hypothetically obtainable from a subject enrolled in a trial but are not obtained. The hypothetically obtainable data consists of every possible observation that could be obtained from a subject from the point of initial screening and randomization to the prespecified scheduled end of follow-up for that subject. In some trials, the prespecified end of study for a subject is a fixed period, such as 1 year of treatment and follow-up. In other trials, the prespecified end may depend on when the subject enters the trial, such as the case in which patient entry is staggered over one period but there is a prespecified date on which all treatment and follow-up will end. If recruitment is conducted over a 3-year period and the total study duration is 5 years, then the first subject randomized hypothetically can contribute 5 years of data collection whereas the last can only contribute 2 years. Thus, for every clinical trial design, each randomized subject has an associated hypothetical complete set of data that could be collected, and the aggregate over all subjects is the set of hypothetically obtainable data.
Data may be missing for many possible reasons or mechanisms, some of which may be ignorable, occur randomly, or occur completely by chance. Missing data that develop from an ignorable mechanism are called missing completely at random (MCAR) [10], in the sense that the unobserved value of the missing observation is statistically independent of other potentially observable information, most importantly including the treatment group assignment. In the context of survival analysis, the equivalent assumption is censoring at random.
Few missing data mechanisms satisfy the MCAR criterion on face value. One is administratively missing data, where data from a subject cannot be obtained because of administrative curtailment of follow-up. This situation usually applies in the setting of staggered patient entry with a fixed study end date, such as the last patient entered in the above example for whom at most 2 years of data could be collected before study end, and for whom the assessments during years 3–5 would be administratively missing.
Missing data may occur for many other reasons. Some subjects may die while participating in the study. Others may be withdrawn from therapy because of poor compliance, lack of evidence of a therapeutic effect, or an adverse effect of therapy, and concurrently withdrawn from the study (i.e., with no additional follow-up). Others may be lost to follow-up (so-called dropouts) because of withdrawal of consent, moving away, incarceration, loss of interest, and so on. The fundamental issue is whether these mechanisms can be claimed to be ignorable.
Of these, losses to follow-up are often considered to be missing completely at random, but missing data from such subjects would only be ignorable when effects of treatment, either positive or negative, played no role in the decision to curtail follow-up. This situation might be plausible if examination of the timing and characteristics of such losses are equivalent among the groups and the characteristics of losses versus those who were not lost to follow-up are equivalent. If differences are detected, then it is possible or even likely that the missing data from such subjects are not ignorable. If baseline covariate differences are detected between those lost to follow-up versus those not lost, then a sensitivity analysis that compares groups adjusted for those covariates might provide a less-biased comparison of the treatment groups.
On-study deaths in some circumstances may also be claimed to be ignorable, as in a study of a disease or condition (e.g., topical skin therapy) that has a negligible risk of mortality. However, even in such cases, deaths may not be ignorable if the treatment itself may adversely affect vital organs, such as through hepatotoxicity (liver toxicity). The latter could be a hypothetical concern for any agent that is known to be metabolized and excreted by the liver. Drugs have been discovered that have none of the other preclinical (i.e., animal) findings or clinical findings (e.g., elevated liver enzymes) that would trigger suspicion of hepatotoxicity but in later trials or clinical practice are shown to pose a risk of possibly fatal hepatotoxicity in some patients.
Clearly, subjects withdrawn from treatment and follow-up because of a specific adverse effect would only be ignorable when the adverse effect can be claimed to be statistically independent of the treatment assignment. This result can virtually never be proven. Other subjects withdrawn from treatment and follow-up because of insufficient therapeutic effect are clearly not ignorable.
The fundamental issue is that in all of these cases, it cannot be proven that the missing data or the mechanism (s) for missing data are ignorable or missing completely at random.
16.2.3 Conditionally Ignorable Missing Data
Many statistical methods require the assumption that missing data are missing completely at random to provide an unbiased analysis. However, other methods provide an unbiased analysis under the assumption that missing data are missing at random (MAR). This explanation is somewhat of a misnomer. Under MAR, it is assumed that the missing data are in fact nonignorable in the sense that the probability of being missing may depend on the unobserved value. However, MAR assumes that this dependence is reflected in other information that has been observed. Thus under MAR, it is assumed that the missing data are conditionally independent of the unobserved value, conditioning on the other information that has been observed including treatment assignment.
Clearly, this is a big assumption. For example, a longitudinal analysis that uses a mixed model implicitly assumes that the data that are missing at a follow-up visit are a function of the baseline characteristics and other follow-up observations that preceded it. The treatment group comparison can then be claimed to be unbiased if this relationship applies (i.e., the structural and random model components are correctly specified) and the important covariates have been measured and observed. However, these assumptions cannot be verified.
16.2.4 Potential for Bias
If the data that are missing develop from nonignorable mechanisms, then the missing data can introduce substantial bias in the results. Lachin [8] presents a model for the assessment of the possible bias for an analysis of the difference between two proportions and the pursuant inflation in the type I error probability α. As the proportion of subjects excluded from the analysis increases, the maximum possible bias and the resulting α increase, as expected. Furthermore, as the total sample size increases, the possible bias and α with a given fraction of missing data increase. Consider the simplest case in which all control group subjects are followed, but a fraction of the treated group has missing data, for example, 20%. For a sample size of 200, a bias of 0.05 leads to an α = 0.14086 whereas for N = 800, the same bias leads to an α = 0.38964.
Various analyses can be performed to assess whether the missing at random (conditionally) assumption applies, such as comparing the characteristics of those with missing versus observed data, in aggregate and within groups, and comparing the characteristics of those with missing data between groups. The null hypothesis of such tests is that the missing data are conditionally ignorable within the context of a particular model. The alternative hypothesis is that they are not ignorable and the resulting analysis is biased. Thus, such tests can reject the null hypothesis of ignorable missing data in favor of the alternative of nonignorable missing data, but such tests cannot prove that missing data are ignorable.
In conclusion, although statistical methods can provide an unbiased analysis of virtually any data structure with missing data when certain assumptions apply, and although those assumptions, either MCAR or MAR conditionally, can be tested and rejected, those assumptions can never be proven to apply, and the resulting analysis can never be proven to be unbiased.
Lachin [8] summarized the issue by stating that
the only incontrovertibly unbiased study is one in which all randomized patients are evaluated and included in the analysis, assuming that other features of the study are also unbiased. This is the essence of the intent-to-treat philosophy. Any analysis which involves post hoc exclusions of information is potentially biased and potentially misleading.
16.3 The Intention-to-Treat Design
Thus, an intention-to-treat design makes every attempt to ensure complete follow-up and collection of outcome data for every participant from the time of randomization to the scheduled completion of study, regardless of other developments such as noncompliance or adverse effects of therapy. The International Conference on Harmonization (ICH) document Guidance on Statistical Principles for Clinical Trials [11] provides the following description of the intention-to-treat principle:
The principle that asserts that the effect of a treatment policy can best be assessed by evaluating on the basis of the intention to treat a subject (i.e., the planned treatment regimen) rather than the actual treatment given. It has the consequence that subjects allocated to a treatment group should be followed up, assessed and analyzed as members of that group irrespective of their compliance with the planned course of treatment.
This guidance also states (Section 5.2.1):
The intention-to-treat principle implies that the primary analysis should include all randomized subjects. Compliance with this principle would necessitate complete follow-up of all randomized subjects for study outcomes.
The ICH the Guidance on General Considerations for Clinical Trials [12, Section 3.2.2] also states:
The protocol should specify procedures for the follow-up of patients who stop treatment prematurely.
These principles are the essence of the intent-to-treat design. To conduct a study that provides high confidence that it is unbiased, the extent of missing data must be minimized.
16.3.1 Withdrawal from Treatment Versus Withdrawal from Follow-Up
Every study protocol should include a provision for the investigator to withdraw a subject from the randomly assigned therapy because of possible adverse effects of therapy. However, the intent-to-treat design requires that such subjects should not also be withdrawn from follow-up. Thus, the protocol should distinguish between withdrawal from treatment versus withdrawal from follow-up. To the extent possible, every subject randomized should be followed as specified in the protocol. In fact, it would be advisable that the study protocol not include provision for the investigator to withdraw a subject from the study (i.e., follow-up). The only exceptions to this policy might be the death or incapacitation of a subject or the subject’s withdrawal of patient consent.
In some studies, time to a major clinical event is the primary outcome, such as a major cardiovascular adverse event or overall survival. In these cases, even if the subject withdraws consent to continue follow-up visits, it would also be important to ask the patient to consent to ascertainment of major events and/or vital status.
Furthermore, in long-term studies, patients may withdraw consent and then later be willing to resume follow-up and possibly the assigned treatment where not contraindicated. To allow patient participation to the extent possible, subjects should not be labeled as “dropouts” while the study is under way. Subjects who withdraw consent or who do not maintain contact may be termed inactive, temporarily, with the understanding that any such subject may later become active. The designation of “dropout” or “lost to follow-up” should only be applied after the study has been completed.
16.3.2 Investigator and Subject Training/ Education
Unfortunately, many investigators have participated in clinical trials that were not designed in accordance with this principle. Even though the protocol may state that all patients should continue follow-up to the extent possible, investigators may fail to comply. In studies that have successfully implemented continued follow-up, extensive education of physicians, nurse investigators, and patients has been implemented.
In the Diabetes Control and Complications Trial (DCCT, 1983–1993), the patients and investigators received intensive patient education on the components of the trial and the expectation that they would continue follow-up [13]. Of the 1441 subjects randomized into the study, during the 10 years of study only 32 subjects were declared inactive at some point in time. Of these subjects, 7 later resumed treatment and follow-up. Among the 1330 surviving subjects at study end, only 8 subjects did not complete a study closeout assessment visit. During the trial, 155 of the 1441 patients deviated from the originally assigned treatment for some period (were noncompliant). Virtually all subjects continued to attend follow-up assessment visits, and most resumed the assigned therapy later.
The DCCT was unusual because two multifaceted insulin therapies were being compared in subjects with type 1 diabetes, who must have insulin therapy to sustain life. Therefore, withdrawal from insulin therapy was not an option. In a study comparing a drug versus placebo, the issues are different.
The Diabetes Prevention Program [14] included comparison of metformin versus placebo for preventing the development of overt diabetes among patients with impaired glucose tolerance. Metformin is an approved antihyperglycemic therapy for treatment of type 2 diabetes with known potential adverse effects that require discontinuation of treatment in about 4% of patients, principally because of gastrointestinal effects. The following is the text provided to the investigators to explain to the patient why the study desired to continue follow-up after therapy was withdrawn due to an adverse effect:
When we designed the study we knew that a fraction of patients would not be able to tolerate metformin. You were told this when you agreed to participate in the study. However, we cannot tell beforehand which participants will be able to take metformin, and which will not.
In order to answer the DPP study question as to whether any treatment will prevent diabetes, every participant randomized into the study is equally important. Thus, even though you will not be taking a metformin pill, it is just as important for us to know if and when you develop diabetes as it is for any other participant. That’s why it is just as important to the study that you attend your outcome assessment visits in the future as it was when you were taking your pills.
16.3.3 The Intent-to-Treat Analysis
An intent-to-treat analysis refers to an analysis that includes all available data for all randomized subjects. However, for an intent-to-treat analysis to comply with the intention-to-treat principle, all “available” data should represent a high fraction of all potentially observable data. Thus, an analysis of all randomized subjects, in which a high fraction have incomplete assessments and missing data, deviates from the intention-to-treat principle in its design and/or implementation and therefore is possibly biased.
16.3.4 Intent-to-Treat Subset Analysis
In many studies, multiple analyses are conducted in different sets of subjects. The intention-to-treat “population” is often defined to include all subjects randomized who had at least one dose of the study medication. However, unless the protocol specifies systematic follow-up of all subjects, and a high fraction of the potentially obtainable data is actually obtained, then an analysis of the intention-to-treat population is simply another post hoc selected subgroup analysis that is susceptible to bias because of nonignorable or informatively missing data.
16.3.5 LOCF Analysis
In an attempt to reconstruct a complete data set from incomplete data, a simplistic approach that is now commonly employed is an analysis using the last observation carried forward (LOCF) for each subject with missing follow-up measurements. This method is popular because it makes it seem as though no substantial data are missing. However, the technique is statistically flawed [15,16]. LOCF values would not be expected to provide the same level of information as values actually measured and would not be expected to follow the same distribution. Furthermore, such values will distort the variance/covariance structure of the data so that any confidence intervals or P-values are biased in favor of an optimistic assessment in that the sample size with LOCF values is artificially inflated and the variance of the measures is artificially deflated. The LOCF method has no formal statistical basis and has been soundly criticized by statisticians.
16.3.6 Structurally Missing Data
In some studies, the primary outcome is the observation of a possibly right-censored event time and a secondary outcome is a mechanistic or other longitudinal measure. Often, the follow-up of a subject is terminated when the index event occurs, which causes all subsequent mechanistic measurements to be missing structurally. For example, in the Diabetes Prevention Program, the primary outcome was the time to the onset of type 2 diabetes, and measures of insulin resistance and insulin secretory capacity were obtained up to the time of diabetes or the end of study (or loss to follow-up). Thus, these mechanistic measures were missing beyond the time of diabetes, and it is not possible to conduct a straightforward intention-to-treat analysis to describe the long-term effect of each initial therapy on these mechanistic measures (e.g., the difference between groups at say 4 years in the total cohort of those entered into the study).
16.3.7 Worst Rank Analyses
In some cases, it may be plausible to assume that subjects with missing data because of a prior index event are actually worse (or better) than all those who continue follow-up for a particular measure. For example, subjects who have died can be assumed to have a worse quality of life than any subject who survives. In this case, the subjects with structurally missing data because of such an index event can be assigned a “worst rank” (i.e., a rank worse than that of any of the measures actually observed) [17].
16.4 Efficiency of the Intent-to-Treat Analysis
16.4.1 Power
The intent-to-treat design, which is necessary to conduct a true intent-to-treat analysis, requires the follow-up of all patients, which includes those who failed to comply with the therapy and those who were withdrawn from therapy by personal choice or by the investigator. Thus, the treatment effect observed may be diluted compared with a setting in which all subjects receive the therapy and are fully compliant. However, that comparison is specious. Virtually every agent or intervention will not be applied optimally in every subject in clinical practice. Therefore, an analysis aimed at the treatment effectiveness under optimal conditions is not relevant to clinical practice.
Such an assessment, however, is of interest as a reflection of pharmacological activity, which is the underlying mechanism by which a treatment is purported to have a clinical effect. This mechanism is the justification for the so-called “efficacy subset” or “per-protocol” analysis often conducted in pharmaceutical trials. The phrase “per-protocol” is used when the protocol itself specifies the post hoc exclusions of patients and patient data based on compliance, adverse effects, or other factors that indicate suboptimal treatment. Such a subset analysis is highly susceptible to bias.
Nevertheless, it is instructive to compare the power of an intention-to-treat design and analysis versus an efficacy subset analysis when it is assumed that the latter is unbiased. Using the test for proportions, Lachin [8] showed that there is a trade-off between the increasing sample size in the intent-to-treat analysis versus the larger expected treatment effect in the efficacy subset analysis. However, in some settings the intent-to-treat design and analysis may be more powerful, especially when the treatment may have some long-term beneficial effects that persist beyond the period of therapy. For example, if the treatment arrests progression of the disease, then a subject treated for a period of time who is then withdrawn may still be expected to have a more favorable outcome long-term compared with a subject originally assigned to control. In this case, the intention-to-treat analysis can have substantially more power than the efficacy subset analysis, and it has the advantage that it is far less susceptible to bias.
These issues were borne out in the analysis of the study of tacrine in the treatment of Alzheimer’s disease [18], in which 663 subjects were entered and 612 completed follow-up. However, only 253 continued on treatment. Thus, the intent-to-treat analysis of the 612 evaluated could be compared with the efficacy subset analysis of the 253 “on-therapy completers” as shown in Reference 8. For some outcomes, the intention-to-treat analysis produced results that were indeed significant, whereas the efficacy subset analysis was not.
16.4.2 Sample Size
In the planning of a study, it is common to adjust the estimate of the sample size for losses to follow-up. For a simple analysis of means or proportions, the sample size computed assuming complete follow-up is inflated to allow for losses. For example, to adjust for 20% losses to follow-up (subjects with missing outcome data), the sample size is inflated by the factor 1/0.8, or by 25%.
Such an adjustment allows for the loss of information because of losses to follow-up or missing data. It does not adjust for the potential bias introduced by such losses if the mechanism for the missing data is informative.
16.5 Compliance-Adjusted Analyses
The efficacy subset analysis is a crude attempt to assess the treatment effect had all subjects remained fully compliant. However, if an intention-to-treat design is implemented, then noncompliance and the degree of compliance become outcome measures, which make it possible to conduct analyses that assess treatment group differences in the primary outcomes while taking into account the differences in compliance. Analyses could also be conducted to estimate the treatment group difference for any assumed degree of compliance in the treatment groups [19–21]. However, these methods can only be applied when study outcomes are measured in all subjects, or a representative subset, which includes those who are noncompliant or who are withdrawn from therapy. These methods cannot be applied in cases where follow-up is terminated when a subject is withdrawn from therapy because of noncompliance or other factors.
16.6 Conclusion
The intention-to-treat principle encourages the collection of complete follow-up data to the extent possible under an intention-to-treat design and the inclusion of all data collected for each subject in an intention-to-treat analysis. An analysis of a so-called Intention-to-treat population of all subjects randomized, but without systematic follow-up, is simply another type of post hoc subset analysis that is susceptible to bias.
References
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[11] Food and Drug Administration, Inter national Conference on Harmonization: Guidance on Statistical Principles for Clinical Trials. Federal Register September 16, 1998; 63: 49583–49598.
[12] Food and Drug Administration, International Conference on Harmonization: Guidance on General Considerations for Clinical Trials. Federal Register December 17, 1997; 62: 66113–66119.
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Further Reading
Principles of Clinical Trial Design and Analysis
[1] D. G. Altman, K. F. Schulz, D. Moher, M. Egger, D. Davidoff, D. Elbourne, P. C. Gøtzsche, and T. Lang, for the CONSORT Group, The revised CONSORT statement for reporting randomized trials: explanation and elaboration. Ann. Intern. Med. 2001; 134: 663–694.
[2] P. Armitage, Controversies and achievements in clinical trials. Control. Clin. Trials 1984; 5: 67–72.
[3] D. L. DeMets, Statistical issues in interpreting clinical trials. J. Intern. Med. 2004; 255: 529–537
[4] P. W. Lavori and R. Dawson, Designing for intent to treat. Drug Informat. J. 2001; 35: 1079–1086
[5] G. S. May, D. L. DeMets, L. M. Friedman, C. Furberg, and E. Passamani, The randomized clinical trial: bias in analysis. Circulation 1981; 64: 669–673.
[6] R. Peto, M. C. Pike, P. Armitage, et al., Design and analysis of randomized clinical trials requiring prolonged observation of each patient. I. Introduction and design. Br. J. Cancer 1976; 34: 585–612.
[7] D. Schwartz and J. Lellouch, Explanatory and pragmatic attitudes in therapeutic trials. J. Chron. Dis. 967; 20: 637–648.
Case Studies
[8] G. Chene, P. Moriat, C. Leport, R. Hafner, L. Dequae, I. Charreau, JP. Aboulker, B. Luft, J. Aubertin, J. L. Vilde, and R. Salamon, Intention-to-treat vs. on-treatment analyses from a study of pyrimethamine in the primary prophylaxis of toxoplasmosis in HIV-infected patients. ANRS 005/ACTG 154 Trial Group. Control. Clin. Trials 1998; 19: 233–248.
[9] The Coronary Drug Project Research Group, Influence of adherence to treatment and response of cholesterol on mortality in the Coronary Drug Project. N. Engl. J. Med. 1980; 303: 1038–1041.
[10] P. W. Lavori, Clinical trials in psychiatry: should protocol deviation censor patient data (with discussion). Neuropsychopharm. 1992; 6: 39–63.
[11] P. Peduzzi, J. Wittes, K. Detre, and T. Holford, Analysis as-randomized and the problem of non-adherence: an example from the Veterans Affairs Randomized Trial of Coronary Artery Bypass Surgery. Stat Med. 1993; 12: 1185–1195.
[12] C. Redmond, B. Fisher, H. S. Wieand, The methodologic dilemma in retrospectively correlating the amount of chemotherapy received in adjuvant therapy protocols with disease-free survival. Cancer Treat. Rep. 1983; 67: 519–526.
Alternative Views
[13] J. H. Ellenberg, Intent-to-treat analysis versus as-treated analysis. Drug Informat. J. 1996; 30: 535–544.
[14] M. Gent and D. L. Sackett, The qualification and disqualification of patients and events in long-term cardiovascular clinical trials. Thrombos, Haemostas. 1979; 41: 123–134.
[15] E. Goetghebeur and T. Loeys, Beyond intention-to-treat. Epidemiol. Rev. 2002; 24: 85–90.
[16] Y. J. Lee, J. H. Ellenberg, D. G. Hirtz, and K. B. Nelson, Analysis of clinical trials by treatment actually received: is it really an option? Stat. Med. 1991; 10: 1595–605.
[17] R. J. A. Little, Modeling the drop-out mechanism in repeated-measure studies. J. Am. Stat. Assoc. 1995; 90: 1112–1121.
[18] L. B. Sheiner, Is intent-to-treat analysis always (ever) enough? Br. J. Clin. Pharmacol. 2002; 54: 203–211.