Intention-to-Treat vs Per-Protocol Analysis: A Complete Guide for Clinical Researchers (2026)

Published June 21, 2026  |  Last updated August 10, 2026

A trial can succeed on one analysis and fail on another, and the difference often comes down to a single methodological choice made before a single patient is randomized. Intention-to-treat vs per-protocol analysis is the decision that determines which participants count toward a clinical trial’s headline result, and it shapes everything from regulatory approval odds to whether a manuscript survives peer review at a major journal. Editors reject papers because authors label a dataset “intention-to-treat” when it quietly excludes people who dropped out, or because a per-protocol result gets reported as though it settles the question randomization was designed to answer.

What follows works through both analysis populations at the level of detail a statistical reviewer expects, including a real trial where the two approaches produced opposite headline conclusions, a second real trial illustrating why non-inferiority studies treat per-protocol as more than a footnote, and the CONSORT 2025 reporting rules published this year that now name the analysis population explicitly in the checklist.

Intention-to-Treat, Modified ITT, and Per-Protocol at a Glance

Current ICH and CONSORT guidance shape how the three analysis populations differ in practice, laid out in the table below.

What Intention-to-Treat Analysis Actually Includes

The intention-to-treat principle keeps participants in the group they were randomized to, no matter what happened afterward. That includes people who never swallowed a single pill, patients who crossed over to the opposing arm, anyone who withdrew consent partway through, participants later found ineligible, and cases with major protocol deviations. Assignment locks in at randomization and does not move.

Statistics, not clinical judgment, drives this rule. Randomization spreads known and unknown confounders evenly across groups at baseline. Drop participants because of something that happened after randomization, whether that is non-adherence or withdrawal, and selection bias creeps back in, because the reasons people stop treatment are rarely unrelated to the treatment itself or to their underlying prognosis. Someone who stops an active drug because of side effects is not interchangeable with someone who stops because they moved out of the trial catchment area. Treating both exits identically, by removing them both from the analysis, erases a distinction that matters.

A full intention-to-treat analysis, run properly, handles missing outcome data through imputation rather than simply excluding anyone with a gap in their record. Last observation carried forward has fallen out of favor with regulators. Multiple imputation and mixed-effects models for repeated measures are now the default choice for handling missingness under a plausible missing-at-random assumption. Planning a missing data strategy before a trial starts, not after enrollment closes, is what separates a defensible ITT analysis from an ITT-in-name-only dataset.

What Per-Protocol Analysis Measures Instead

Per-protocol analysis narrows the dataset to participants who completed the trial close to how it was designed. That typically means receiving the assigned treatment at an adequate dose for the required duration, avoiding major protocol deviations, and having outcome data collected at the specified time points. Defining “close to as designed” cannot happen after the data are unblinded. A per-protocol population built after investigators have seen the results is treated by regulators as analytical manipulation rather than methodology, and reviewers look specifically for evidence that the exclusion rules were locked into the statistical analysis plan beforehand.

Per-protocol analysis answers what some methodologists call the explanatory question. If a patient takes a drug exactly as prescribed, does it work biologically? For a vaccine trial, that translates into knowing whether full immunization confers protection, which matters directly for label claims. For an antibiotic trial, it shows whether the drug clears infection when every dose is taken. In both settings per-protocol is not a footnote to the real analysis. It is central to the clinical question being asked.

Its weakness is equally central. Non-adherence and drop-out are almost never random events. Patients who stop a drug because of side effects differ systematically from those who tolerate it well, and patients who withdraw because their disease is progressing differ systematically from those who complete follow-up in good health. Remove those participants and the two arms are no longer the balanced groups randomization created. Per-protocol estimates therefore skew optimistic more often than not, because the per-protocol population has effectively been pre-selected for both the capacity to adhere and, frequently, a better underlying prognosis.

Modified Intention-to-Treat and the ICH E9(R1) Estimand Framework

Modified intention-to-treat sits between the two extremes. It keeps every randomized participant except those excluded under criteria that were clinically justified and locked in before unblinding. Typical mITT exclusions remove participants who never received a single dose of study drug, participants found not to meet eligibility criteria after randomization, and participants lost to follow-up before any post-baseline assessment took place.

Regulators accept mITT under three conditions. Exclusions must be pre-specified rather than discovered conveniently after the data come in. The excluded share of the randomized population should stay small, generally under five to ten percent. And the exclusion criteria cannot correlate with treatment assignment or with prognosis. ICH E9(R1) actually recommends abandoning the “mITT” label altogether in favor of describing the analysis population directly and naming which intercurrent events were handled and how, tied to a formally defined estimand.

An estimand is built from five components, the population being studied, the outcome variable, the treatments being compared, how intercurrent events are handled, and the summary measure used to express the comparison. ICH E9(R1) lays out four strategies for handling an intercurrent event such as non-adherence.

• Treatment policy strategy. Count the intercurrent event as part of the outcome, which is effectively what a full ITT analysis does.
• Hypothetical strategy. Estimate what would have happened had the intercurrent event not occurred at all.
• Principal stratum strategy. Restrict the analysis to the subgroup of participants for whom the event would not have occurred, conceptually close to per-protocol.
• Composite strategy. Fold the intercurrent event itself into how the outcome is defined.

A protocol written under this framework states up front which estimand the trial targets and which analysis implements it, rather than leaving readers to reverse-engineer the answer from a results table. Randomized controlled trial design choices made at the protocol stage, including this one, are far cheaper to get right before enrollment than to patch after the data are in.

A Real Trial Where Intention-to-Treat and As-Treated Analysis Disagreed

CABANA trial data illustrate this well. The trial randomized 2,204 patients with atrial fibrillation to catheter ablation or drug therapy and has become a standard teaching case for what happens when adherence and crossover run high. Its intention-to-treat result showed no statistically significant advantage for ablation on the primary composite endpoint of death, disabling stroke, serious bleeding, or cardiac arrest, at 8.0 percent for ablation versus 9.2 percent for drug therapy (hazard ratio 0.86, 95% CI 0.65 to 1.15).

Crossover in this trial was substantial enough to matter. Roughly 9 percent of patients assigned to ablation never actually had the procedure, while about 28 percent of patients assigned to drug therapy crossed over and received ablation anyway during follow-up. Regrouping patients by the treatment they actually received changed the picture considerably. An as-treated analysis showed a significant reduction in the primary endpoint for ablation, at 7.0 percent versus 10.9 percent (hazard ratio 0.67, 95% CI 0.50 to 0.89).

Terminology matters here. CABANA’s supportive analysis was as-treated, meaning patients were regrouped by what they actually received regardless of assignment, which differs from a strict per-protocol analysis that would exclude crossover patients rather than reclassify them. Both approaches sacrifice the protection randomization provides, and both run a higher bias risk than the ITT result, which is exactly why the trial’s published conclusion rests on the intention-to-treat hazard ratio and treats the as-treated finding as hypothesis-generating rather than confirmatory. A clinician who read only the as-treated number would walk away with a substantially rosier impression of ablation than the trial as a whole supports.

Why Non-Inferiority Trials Need Both Intention-to-Treat and Per-Protocol

Superiority trials and non-inferiority trials handle non-adherence in opposite directions, and that asymmetry is the single most important exception to “ITT is always primary” in the entire field. In a superiority trial, non-adherence dilutes a real treatment effect toward zero, so intention-to-treat gives the conservative, cautious answer. In a non-inferiority trial the logic flips. Diluting a real difference toward zero makes two unequal treatments look more alike, which can push a trial toward incorrectly concluding non-inferiority. Sloppy conduct, in other words, can masquerade as a successful result. A 2024 simulation study built on real non-inferiority trial data found that both intention-to-treat and per-protocol analyses can produce biased estimates once non-adherence differs meaningfully between arms, which is precisely why neither approach alone is considered sufficient in this trial design.

REMoxTB, a tuberculosis treatment trial, shows both the risk and the safeguard in action. Investigators randomized 1,931 patients to a standard six-month regimen or one of two experimental four-month, moxifloxacin-containing regimens, and reported both a per-protocol and a modified intention-to-treat analysis rather than picking one. Favorable outcomes in the per-protocol population reached 92 percent in the control arm compared with 85 percent and 80 percent in the two experimental arms. Modified intention-to-treat data told a consistent story, at 84 percent for control against 77 percent and 76 percent for the experimental regimens. Neither analysis supported non-inferiority for either four-month regimen, and because the two approaches agreed, reviewers could be confident the negative result was not an artifact of which population got analyzed.

Agreement between ITT and per-protocol is itself informative, and it is what regulators want to see in a non-inferiority submission, because divergence between the two raises exactly the false-equivalence concern this section describes. OVIVA, which tested oral against intravenous antibiotics for bone and joint infection in 1,054 patients, offers a cleaner example of concordance working in the treatment’s favor. Both its intention-to-treat and its per-protocol populations supported non-inferiority of oral therapy, with treatment failure running at roughly 14 percent on intravenous therapy against 13 percent on oral therapy in the full randomized cohort, and a similar pattern in the smaller per-protocol population. A non-inferiority claim resting on concordant ITT and per-protocol results, as OVIVA’s does, carries far more weight than one resting on either analysis alone.

CONSORT 2025 and the New Reporting Requirements for Your Analysis Population

CONSORT was rebuilt this year for the first time since 2010, and the new version speaks directly to the intention-to-treat versus per-protocol question in language the 2010 checklist never used explicitly. Hopewell and colleagues published CONSORT 2025 simultaneously in BMJ, JAMA, The Lancet, and Nature Medicine, expanding the checklist from 25 items to 30 and adding a dedicated open science section covering registration, protocol access, and data sharing.

For analysis populations specifically, Item 21b now requires authors to define each analysis population explicitly, naming whether a given result reflects intention-to-treat, per-protocol, or another population, and stating who is included and in which group. Item 21c requires a clear account of how missing data were handled. Neither requirement is new in spirit. Careful trialists have done both for years. What changed is that CONSORT no longer leaves this to author discretion buried inside general statistical-methods language. A journal editor checking a submission against the CONSORT 2025 checklist can now flag a paper specifically for failing to define its analysis population, a softer and easier-to-miss failure mode under the 2010 wording.

Writing this section of a methodology section well means stating the analysis population before presenting a single result, not defending it retroactively in the discussion after a reviewer asks.

Choosing the Right Analysis for Your Trial Design

Trial design, more than habit, determines the right primary analysis. Current practice across regulatory superiority trials, non-inferiority trials, vaccine studies, and pragmatic surgical or behavioral trials appears in the table below.

Trial designs that involve repeated dosing periods, such as a crossover design, add their own wrinkles to this table, since a participant can be non-adherent in one period and fully adherent in the next.

Common Mistakes That Undermine an ITT Claim

Reviewers count. That is the single most common way an “ITT” claim falls apart under scrutiny. If the number analyzed is smaller than the number randomized, something got excluded, and a paper that does not explain what and why invites suspicion rather than trust. A second frequent error is finalizing per-protocol exclusion criteria after unblinding, which regulators and statistical reviewers treat as a red flag regardless of how reasonable the criteria sound in isolation. Exclusion rules belong in the statistical analysis plan, locked before anyone sees which arm did better. A third and increasingly dated practice is defaulting to last observation carried forward for missing data in an ITT analysis. Multiple imputation or mixed-effects models for repeated measures are now the expected standard, and a submission built on LOCF without sensitivity analyses around that choice will draw methodological objections at peer review before the science even gets discussed.

Protocol deviations deserve their own scrutiny too. A trial that fails to log and report protocol deviations systematically cannot credibly define a per-protocol population later, because the exclusion criteria have nothing consistent to point to. Documenting deviations as they happen, not reconstructing them from memory during analysis, is what makes a per-protocol dataset defensible rather than convenient.

Journal and Regulatory Requirements in 2026

JAMA requires disclosure of the primary analysis population in the Methods section, along with a statement of whether any randomized participants were excluded and why. NEJM requires a CONSORT flow diagram for parallel-group trials, and that diagram now needs to reconcile with whichever flow diagram convention the journal follows. For regulatory submissions, the FDA expects the primary efficacy dataset to be the ITT or mITT population. EMA’s clinical pharmacology guidance on estimands operationalizes ICH E9(R1) for marketing authorization applications, making estimand disclosure a formal part of Module 5 of the CTD dossier.

Frequently Asked Questions

What is the difference between intention-to-treat and per-protocol analysis?
Intention-to-treat analyzes every randomized participant according to the group they were assigned to, adherence aside, which preserves the balance randomization created. Per-protocol restricts the analysis to participants who completed the trial largely as designed, which estimates efficacy under close to ideal conditions but reopens the door to selection bias.

Why is intention-to-treat the default primary analysis?
Because it keeps randomization intact. Excluding participants based on what happened after randomization, non-adherence included, breaks the balance between groups that randomization was designed to guarantee. ICH E9(R1) treats intention-to-treat, or a clearly defined equivalent under the treatment policy strategy, as the standard primary approach for confirmatory superiority trials.

When should per-protocol results be reported alongside intention-to-treat?
Always, as a sensitivity or supportive analysis rather than a replacement. It becomes especially important in non-inferiority trials, where both are effectively co-primary, in vaccine trials assessing efficacy under confirmed immunization, and in any trial where a label claim depends on outcomes under full adherence.

What is modified intention-to-treat and do regulators accept it?
Modified intention-to-treat excludes a small, pre-specified share of randomized participants, commonly under ten percent, based on criteria fixed before unblinding, such as never receiving a single dose. Regulators accept it when the exclusions are pre-specified, clinically justified, small, and unrelated to treatment assignment or prognosis. ICH E9(R1) actually prefers that authors skip the “mITT” label and describe the analysis population directly instead.

What does it mean when intention-to-treat and per-protocol results disagree?
It signals that non-adherence or drop-out was not random, meaning the people who left the trial differed systematically from those who stayed. CABANA is the clearest documented example, where the intention-to-treat hazard ratio showed no significant benefit for ablation while the as-treated analysis showed a significant one. The intention-to-treat result is treated as the primary finding, and a favorable per-protocol result on its own does not rescue a trial that misses on intention-to-treat.

Is an as-treated analysis the same thing as a per-protocol analysis?
No, though the two get used interchangeably in casual writing. Per-protocol excludes participants who deviated from the assigned protocol. As-treated regroups every participant by the treatment they actually received, crossovers included, regardless of assignment. Both move away from the randomized groups and both carry more bias risk than intention-to-treat, but they answer subtly different questions and a careful manuscript should not conflate them.

Does CONSORT 2025 require both intention-to-treat and per-protocol to be reported?
CONSORT 2025 Item 21b requires every analysis population to be explicitly named and defined, whichever one a trial reports. For non-inferiority trials both intention-to-treat and per-protocol are expected. For superiority trials intention-to-treat must be reported, and per-protocol is strongly recommended as a sensitivity analysis by most major journals and virtually all regulatory agencies.

References

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Editverse Research Team | Updated August 2026