What is intention-to-treat analysis?

Intention-to-treat analysis compares participants in the trial groups to which they were randomly assigned, regardless of the treatment they actually received, their adherence, or whether they completed the protocol. Analysing as randomised preserves the prognostic balance randomisation created, so the estimate answers what happens when a treatment is offered — not what happens when it is taken.

That definition is uncontroversial and almost every trial claims to follow it. The difficulty is that intention-to-treat is three separate requirements wearing one name, that trials routinely satisfy two of them and fail the third, and that regulators have spent the last decade replacing the label with something more precise. This page covers what the principle requires, what the estimate means, why adherence cannot define an analysis group, where intention-to-treat stops being the safe choice, how the estimands framework reframed it, how a broken implementation is detected in a manuscript, and what reviewers say when it has been mishandled.

What intention-to-treat requires

ICH E9, the harmonised guideline on statistical principles for clinical trials dated 5 February 1998, defines the intention-to-treat principle in its glossary: “The principle that asserts that the effect of a treatment policy can be best 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 analysed as members of that group irrespective of their compliance to the planned course of treatment.”

ICH E9(R1), the estimands addendum adopted on 20 November 2019, unpacks that sentence into three consequences that are usually collapsed into one.

All participants relevant to the research question are included. The analysis set starts from everyone randomised, not everyone treated, not everyone who returned for a visit.

Participants are analysed in the group to which they were randomised. Where a dispensing error gives a participant the other arm’s treatment, that participant stays in the arm the randomisation list assigned.

Participants are followed up and assessed regardless of adherence, and those assessments are used in the analysis. This third consequence is operational rather than analytical: it is a demand on trial conduct, made before the database is locked, and it is the one trials fail.

ICH E9 gives the operational set a separate name, because the ideal is rarely reached exactly. The full analysis set is defined in the same glossary as “the set of subjects that is as close as possible to the ideal implied by the intention-to-treat principle. It is derived from the set of all randomised subjects by minimal and justified elimination of subjects.” A manuscript that says “intention to treat” and reports the full analysis set is being ordinarily imprecise; a manuscript that says “intention to treat” and reports neither is being misleading.

What the estimate means

Intention-to-treat estimates the effect of a treatment policy — what happens to a population offered the assigned treatment under the conditions of the trial, including the discontinuation, switching and rescue medication that actually occurred. That is a different quantity from the effect of the drug on the people who take it as directed, and the gap between them is not error.

Consider a drug that reduces events substantially in those who tolerate it, and that 40% of participants abandon within three months because of nausea. The intention-to-treat estimate will be modest. The estimate among adherent participants will be large. Both numbers describe something real: the first describes what a health system that adopts the drug should expect, the second describes what a patient already six months into treatment without nausea should expect. Neither is the “true” effect with the other as its distortion.

ICH E9(R1) states the limitation of the principle in its own purpose and scope section rather than leaving it to critics: “It remains undisputed that randomisation is a cornerstone of controlled clinical trials and that analysis should aim at exploiting the advantages of randomisation to the greatest extent possible. However, the question remains whether estimating an effect in accordance with the ITT principle always represents the treatment effect of greatest relevance to regulatory and clinical decision making.” Papers that treat intention-to-treat as the answer rather than as one clearly defined question have skipped the sentence a regulator wrote about its own guidance.

A further distinction specialists draw, and manuscripts routinely blur, is between the estimand and the estimator. The estimand is the treatment-policy quantity itself — what intention-to-treat targets. The estimator is the calculation that produces a number for it: a mixed model for repeated measures fitted to all observed data, or a multiple-imputation analysis, can both target the same treatment-policy estimand. Under data missing at random the two typically converge; under data missing not at random they can diverge, because each makes a different assumption about the unobserved values. Stating the estimand does not specify the estimator, and a methods section that names one without the other has described only half the analysis.

Common questions about intention-to-treat analysis

What does intention-to-treat actually mean?

Intention-to-treat means analysing every participant in the group they were randomly assigned to, whatever treatment they actually received and however well they followed the protocol. It is not a statistical test but a rule for building the analysis population: keep the randomised groups intact so the comparison still reflects random assignment rather than what happened afterwards.

Is ITT the same as analysing everyone who got the drug?

No, and this is the most common mix-up. Analysing everyone who received a given treatment — an as-treated analysis — groups participants by what they took, not by what they were assigned, and discards randomisation entirely. Intention-to-treat keeps a participant in their assigned arm even when a dispensing error gave them the other arm’s treatment.

If patients dropped out of my trial, can I still call my analysis intention-to-treat?

Only if you kept them in their randomised arm and, ideally, still have their outcome data. Dropout and non-adherence do not disqualify a comparison from being intention-to-treat as long as participants are analysed as randomised. What does disqualify it is losing the outcome itself: a participant with no recorded outcome is a missing-data problem, covered below, that grouping alone cannot fix.

Why adherence cannot define an analysis group

Adherence is measured after randomisation and is strongly prognostic, which is why grouping participants by whether they adhered destroys the property that makes a trial a trial.

The Coronary Drug Project supplied the demonstration that settled this in 1980. Within the placebo arm alone, five-year mortality was about 15% among the 1,813 participants who took at least 80% of their assigned capsules and about 28% among the 882 who did not. Placebo capsules do not prevent death. The gap measured how the sort of person who adheres differs from the sort who does not, and adjustment for 40 recorded baseline characteristics reduced the difference only to 9.4 percentage points. The residual is confounding by variables the trial never recorded.

The 1980 result circulates as proof that adherence adjustment is impossible in principle. Murray and Hernán’s 2016 reanalysis of the same data in Clinical Trials is the honest correction: using inverse probability weighting to handle post-randomisation predictors of adherence rather than baseline covariates alone, the placebo-arm difference was substantially attenuated and its confidence interval included no difference at all. The durable lesson is narrower than the folklore. Naive adherence adjustment fails badly; adjustment for time-varying confounders affected by prior treatment is a live methodological programme with published estimators, not an impossibility. What remains true without qualification is that a simple comparison of adherent treated participants with adherent control participants is an observational study conducted inside a randomised trial, and that conditioning on a post-randomisation variable influenced by both arm and outcome can introduce collider bias on top of the confounding.

Questions about per-protocol analysis and dropouts

Why can’t I just drop the patients who didn’t follow the protocol?

Because dropping them turns a randomised comparison into an observational one. Whether a participant adheres is measured after randomisation and is itself associated with prognosis, so restricting to adherent participants in both arms reintroduces the selection that randomisation was designed to remove — the Coronary Drug Project’s placebo-arm result is the standard demonstration.

Is complete-case analysis the same thing as an ITT analysis?

No. Complete-case analysis silently redefines the analysis population as everyone who happened to supply an outcome, which is a post-randomisation, outcome-dependent selection. A genuine intention-to-treat analysis starts from everyone randomised; complete-case analysis is one specific, usually unstated, way of handling the missing-data problem intention-to-treat does not itself solve.

What’s the actual difference between ITT and per-protocol?

Both group participants by randomised assignment, so neither is a return to as-treated analysis. The difference is who is included: intention-to-treat keeps everyone randomised, while per-protocol excludes participants with major protocol deviations. That exclusion is adherence-related and therefore reintroduces confounding, which is why per-protocol is a secondary analysis, not a substitute primary one.

Where intention-to-treat is not the conservative choice

Non-inferiority and equivalence trials invert the usual argument for intention-to-treat analysis. ICH E9 section 5.2.3 states the reversal without hedging: “in an equivalence or non-inferiority trial use of the full analysis set is generally not conservative and its role should be considered very carefully.”

The mechanism is direct. Non-adherence, discontinuation and switching push both arms towards the same observed outcome distribution, and two arms looking alike is the finding a non-inferiority trial is designed to produce. A poorly conducted non-inferiority trial therefore returns a more favourable result than a well conducted one, and intention-to-treat provides no protection against this because dilution is the direction of its bias.

The regulatory literature ties this to a second, distinct requirement for active-control trials: assay sensitivity, a trial’s ability to distinguish an effective treatment from an ineffective one, addressed in ICH’s guidance on choice of control group. A non-inferiority trial can lose assay sensitivity for reasons that have nothing to do with which analysis population is reported — a weak or inconsistently dosed control arm, poor adherence in both arms, or lax outcome ascertainment. Per-protocol analysis is one check against dilution bias, not a substitute for those design safeguards; a manuscript that adds a per-protocol analysis but shows no evidence the trial could have detected a true difference (a failed active-control arm, for instance) has not answered the assay-sensitivity question at all.

The corresponding claim for superiority trials is weaker than usually stated. ICH E9 says “in many clinical trials the use of the full analysis set provides a conservative strategy” — “many”, not all, and conservative only towards the null in the direction the trial hypothesised. Where outcome data are missing differentially by arm, where a treatment harms a subgroup, or where control participants obtain the active treatment outside the protocol, the intention-to-treat estimate can be biased in either direction.

ICH E9’s remedy is to run both and pre-specify both: “In confirmatory trials it is usually appropriate to plan to conduct both an analysis of the full analysis set and a per protocol analysis, so that any differences between them can be the subject of explicit discussion and interpretation.” A manuscript reporting only one of the two in a non-inferiority setting has an unanswered question at its centre.

Missing outcome data is the failure intention-to-treat cannot absorb

Missing outcome data breaks intention-to-treat in a way that non-adherence does not. Analysing as randomised protects the comparison only when an outcome exists for everyone randomised; a participant with no recorded outcome contributes nothing to the estimate, so the set actually analysed is defined by a post-randomisation event — whether the person came back.

Hollis and Campbell measured how common this is in the BMJ in 1999. Of 249 randomised trial reports published in 1997 in the BMJ, the Lancet, JAMA and the New England Journal of Medicine, 119 (48%) mentioned intention-to-treat analysis, and 89 of those 119 — 75% — had missing data on the primary outcome variable. The label, in other words, was most often applied to analyses that could not have satisfied it, and the review found reports that excluded participants who never started the allocated intervention or analysed them outside their randomised group while still claiming the term.

Two common handlings do not qualify as intention-to-treat whatever the methods section calls them. Complete-case analysis silently redefines the population as those who supplied an outcome. Last observation carried forward imputes a value and then reports a confidence interval computed as though the value had been observed, understating uncertainty; it is not conservative either, because in a condition that progresses, carrying a baseline value forward flatters whichever arm deteriorates faster.

ICH E9 puts the remedy in trial conduct rather than in analysis: measurements collected at the point of loss to follow-up, or subsequently in line with the protocol schedule, “are valuable in this context; subsequent collection is especially important in studies where the primary variable is mortality or serious morbidity. The intention to collect data in this way should be described in the protocol.” Where data are missing regardless, a stated missing-data assumption, a model-based or multiple-imputation analysis aligned to it, and sensitivity analyses under departures from that assumption are the defensible minimum.

Frequently asked questions about missing data and modified ITT

Can I use last observation carried forward (LOCF) for my primary endpoint?

Using LOCF is defensible only if you can justify why the last observed value is a reasonable stand-in for the missing one, and reviewers increasingly ask for that justification explicitly. It also is not conservative by default: in a condition that progresses over time, carrying an early value forward flatters whichever arm is deteriorating faster, and it understates uncertainty by treating an imputed value as if it had been observed.

What does modified intention-to-treat (mITT) mean, and is it legitimate?

Modified intention-to-treat has no single standard definition — published trials use it for participants who received at least one dose, who had one post-baseline assessment, or who passed eligibility review, often in combination. It is legitimate only when the exclusion rule is stated explicitly with the number excluded per arm, and only when that rule could have been applied without knowing how treatment went.

My reviewer wants a sensitivity analysis for missing data — what does that mean in practice?

It means showing the primary result still holds under a less favourable assumption about the missing values, not merely under the one you chose. Common approaches include tipping-point analysis (finding how extreme the missing outcomes would need to be to overturn the result) and pattern-mixture or delta-adjusted multiple imputation, which shift imputed values away from the primary assumption by a stated amount.

The exclusions ICH E9 permits, and what “modified” means

ICH E9 names a short and explicitly limited set of post-randomisation exclusions from the full analysis set: failure to satisfy major entry criteria, failure to take at least one dose of trial medication, and the absence of any data after randomisation. The guideline introduces them as “a limited number of circumstances … including” these three, so the list constrains rather than closes. Each “should always be justified”.

For eligibility violations the guideline sets four conditions that must all hold before exclusion can be made “without the possibility of introducing bias”: “(i) the entry criterion was measured prior to randomisation; (ii) the detection of the relevant eligibility violations can be made completely objectively; (iii) all subjects receive equal scrutiny for eligibility violations; (iv) all detected violations of the particular entry criterion are excluded.” Condition (iii) is the one open-label trials fail, because unblinded investigators do not scrutinise both arms equally.

“Modified intention to treat”, abbreviated mITT, is the label trials attach to the resulting set, and it has no standard definition. Published trials use it for participants who received at least one dose, who had at least one post-baseline assessment, who met eligibility on central review, or some combination; the systematic review by Abraha and Montedori in the BMJ in 2010 catalogued the variety and the inconsistency. An mITT label is therefore uninformative on its own: a manuscript must state the exclusion rule and the number excluded per arm, or it has reported nothing about its analysis population.

One test separates a defensible mITT from a broken one. Ask whether the exclusion criterion could have been evaluated without knowing the assignment and without waiting to see how treatment went. “Received no dose” often passes, provided the decision not to dose could not be influenced by knowledge of assignment. “Had at least one post-baseline efficacy assessment” almost never passes, because whether a participant returns for assessment depends on how the treatment went.

Intention-to-treat under the estimands framework

ICH E9(R1), adopted on 20 November 2019, replaced the binary choice between intention-to-treat and per protocol with five named strategies for handling intercurrent events — discontinuation, treatment switching, use of rescue medication, death. Intention-to-treat corresponds to the treatment policy strategy, defined verbatim as: “The occurrence of the intercurrent event is considered irrelevant in defining the treatment effect of interest: the value for the variable of interest is used regardless of whether or not the intercurrent event occurs.”

The other four strategies are named alongside it, not beneath it — each is a legitimate, fully specified alternative for a given intercurrent event, not a fallback for when treatment policy is inconvenient. The hypothetical strategy targets the value that would have been observed had the intercurrent event not occurred. The composite variable strategy folds the event itself into the outcome definition, so a discontinuation becomes part of what is measured rather than something to be handled around it. The while on treatment strategy uses only the values recorded up to the event. The principal stratum strategy restricts the estimand to the subpopulation who would not have experienced the event under either assignment — the same logical move as the complier average causal effect described below, applied to a broader class of intercurrent events. A protocol should name which of the five applies to each intercurrent event it anticipates; “the analysis was intention to treat” cannot express a mixed choice across events.

Three consequences follow for how a trial manuscript should read.

One trial can use different strategies for different intercurrent events. Treatment policy for rescue medication and a hypothetical strategy for a treatment switch is a coherent, fully specifiable choice; “the analysis was intention to treat” cannot express it.

Treatment policy is unavailable for terminal events. ICH E9(R1): “In general, the treatment policy strategy cannot be implemented for intercurrent events that are terminal events, since values for the variable after the intercurrent event do not exist.” A symptom score after death does not exist, so “we analysed by intention to treat” is not an answer to how deaths were handled — a composite variable, a while-on-treatment strategy or a competing-risks formulation is.

Reporting standards have moved from the label to the definition. CONSORT 2010’s item 16 asked, for each group, for the number of participants included in each analysis and “whether the analysis was by original assigned groups” — a question a paper can answer with the phrase alone. The 2025 update asks instead for a definition of who is included in each analysis and the group in which participants were analysed, and asks separately for the number analysed and the number with available outcome data. Those last two numbers are the useful pair: their difference is exactly the quantity that imputation conceals, and no label reveals it.

Intention-to-treat and the analyses it is contrasted with

Intention-to-treat is one of five analysis populations a trial may report, and the distinctions are about who is counted and how they are grouped, not about statistical technique.

The complier average causal effect deserves one clarification, because it is frequently described as “per protocol done properly”. Instrumental-variable estimation using randomised assignment as the instrument recovers an unbiased effect for a subgroup — those who would comply whichever arm they were assigned to — that cannot be identified in the data, and it requires an exclusion restriction (assignment affects the outcome only through treatment received) and monotonicity (no participant does the opposite of their assignment) that are assumptions, not findings. It is a legitimate secondary analysis with named conditions, not a repair for a diluted primary result.

One further population sits outside this table because it answers a different kind of question: the safety population, conventionally every participant who received at least one dose, analysed as treated regardless of randomised assignment. Convention in trial reporting treats this as the default population for adverse-event tables precisely because safety reporting is descriptive rather than causal — an adverse event is attributed to the drug a participant actually took, so the as-treated grouping that would bias an efficacy comparison is exactly the grouping a safety table needs. A manuscript that reports intention-to-treat for efficacy and as-treated for safety in the same paper is not being inconsistent; using as-treated for both would be.

How a broken intention-to-treat analysis is detected in a manuscript

A broken intention-to-treat analysis is found by arithmetic before it is found by judgement, and five checks catch most failures.

Reconcile every denominator against the randomised total. Take the number randomised per arm from the participant flow diagram, then read every table, figure caption and reported rate and record the denominator each one uses. Any denominator smaller than the randomised total requires a matching entry in the flow diagram’s post-randomisation exclusions, with a reason.

Check whether denominators move between outcomes. A trial with a single analysis population has one denominator per arm. Denominators that differ across outcomes indicate per-outcome complete-case analysis, which is a different population for each result and rarely acknowledged as such.

Read the population definition against the numbers rather than against the label. A methods section stating “all randomised participants were analysed” alongside a results table with a smaller n is an internal contradiction that survives peer review with some regularity.

Look for participants moved between arms. A flow diagram showing that participants were “analysed in the group they received” contradicts an intention-to-treat claim in the same paper, and the contradiction is visible without any subject knowledge.

Check ascertainment for participants who stopped treatment. Trials that discontinue follow-up at treatment discontinuation cannot produce an intention-to-treat estimate at all, because the third requirement — assess regardless of adherence — was violated before analysis began. The tell is a discontinuation count that matches the missing-outcome count.

Confirm the unit of randomisation matches the unit of analysis. In a cluster-randomised trial, “analysed as randomised” means analysed by cluster assignment with the non-independence of participants within a cluster accounted for — an intention-to-treat label attached to an analysis that treats individually clustered participants as independent observations has not fixed the problem the clustering created; it has stated the wrong population correctly while getting the variance wrong.

PerfectPaper reconciles every reported denominator against the number randomised and reports each analysis whose population is named but not defined. The same reconciliation catches the related defect in single-arm and response-rate reporting, which the response criteria discipline agent covers for oncology manuscripts.

What reviewers say

Reviewer objections to a mishandled intention-to-treat analysis are unusually formulaic, which makes them easy to anticipate. The phrasings below are the ones that recur across trial reports.

“The analysis is described as intention to treat, but the denominators in Table 2 are smaller than the numbers randomised.” “Please clarify how participants who discontinued study treatment were followed and analysed.” “The term modified intention to treat is used without a definition; please state the exclusion criteria and the number excluded in each arm.” “Given the non-inferiority design, a per-protocol analysis is required in addition to the primary analysis.” “Missing outcome data appear to have been handled by complete-case analysis; please justify the missing-at-random assumption and present a sensitivity analysis.” “Participants appear to have been analysed according to treatment received rather than as randomised.”

The last is the one that decides papers. Analysing as treated is not a reporting flaw a revision can rephrase; it is a different study design, and the reviewer asking about it is asking for a reanalysis.

Common questions about reviewer pushback on ITT

My reviewer says my ITT analysis doesn’t match my per-protocol results — what should I say?

Say what the discrepancy means rather than explaining it away: the two estimate different things, so disagreement is expected, not a red flag by itself. What you need to address is direction and size — a large gap that favours the treatment more under per-protocol than under intention-to-treat is consistent with non-adherence diluting the primary estimate, and you should say so explicitly rather than let the reviewer infer it.

Why did my p-value change when I switched from per-protocol to intention-to-treat?

Because intention-to-treat includes non-adherent and discontinued participants whose outcomes trend toward no effect, which dilutes the treatment difference under a superiority design — so the p-value usually moves toward the null. In a non-inferiority trial the same dilution moves both arms toward looking alike, which can shift the p-value the opposite, more favourable way — why ICH E9 asks for both analyses there specifically.

Contested points and limitations

Several claims about intention-to-treat are stated as settled in textbooks and are not.

“Intention-to-treat is conservative” is true only in a restricted sense. It biases towards the null in a superiority trial when the treatment works in the hypothesised direction and outcomes are complete. It is anti-conservative in non-inferiority and equivalence designs, by ICH E9’s own statement, and unpredictable when missingness differs by arm.

Intention-to-treat does not deliver an unbiased effect when outcomes are missing. The principle preserves randomisation across the randomised set, not across the analysed set. No labelling convention repairs a trial with 30% loss to follow-up.

Intention-to-treat says nothing about external validity. The estimate applies to the trial’s enrolled population under the trial’s conditions. Whether it transports to routine care is a separate argument requiring separate evidence.

Cluster-randomised trials have a failure mode intention-to-treat cannot address. Where clusters are randomised before individual participants are identified and recruited, and recruiters know the cluster’s assignment, the participants entering each arm may differ systematically. Analysing as randomised preserves nothing if the arms were populated differently, and the non-independence of observations within clusters is a separate issue again.

Whether intention-to-treat should be the primary estimand is genuinely open. ICH E9(R1) declines to settle it, and pragmatic trials answering health-system questions and explanatory trials answering biological questions have different defensible answers. What is not open is that the choice must be stated, defined and pre-specified.

How to report intention-to-treat

Report the intention-to-treat analysis by content rather than by label. State the number randomised per arm, the number analysed for each outcome, the number with observed outcome data, and any difference between the last two attributable to imputation. Report post-randomisation exclusions with reasons and per-arm counts, and say whether the exclusion criterion was evaluable without knowledge of assignment.

State how each intercurrent event was handled, separately, using ICH E9(R1)’s vocabulary where the trial was designed within it. State the missing-data assumption in words a reader can disagree with, and present at least one sensitivity analysis that departs from it. Where a per-protocol or complier-average analysis is reported alongside, say which was pre-specified as primary and present both estimates in the abstract if they differ materially, rather than letting the abstract carry the more favourable one. Trials with an unusual analysis population should confirm it against the registered protocol before submission, which is also where endpoint pre-specification is checked.

Related

Confounding · Collider bias · Immortal time bias · Reviewer objections about statistics · Research methods concepts

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