Interval-Censored Endpoints: Keep Both Observation Bounds in Trial Analysis

In a prevention trial, a participant tests negative at the scheduled month 12 visit and positive at month 15. Data management and biostatistics then face a recurring question: what single event date should enter the time-to-event dataset? The month 15 detection date? The 13.5-month midpoint? The honest answer is that neither date was observed. The event occurred at some unknown time T in the interval (L, R], where L is the last documented negative assessment and R is the first confirmed positive one.

Collapsing that interval into one date turns an artifact of the visit schedule into apparent clinical data. Treating the first-positive date as exact in Kaplan-Meier or Cox analyses is documented to bias the survival curve, and the bias grows when assessments are infrequent or differ between arms; midpoint and first-detection imputation are both reported to be biased and less efficient than interval-aware methods. The practical rule: keep both observation bounds, L and R, as analysis variables. The ICH E9(R1) addendum does not discuss interval censoring, but it requires the variable (endpoint) to be precisely specified as an estimand attribute. In our reading, that puts interval handling in the prespecified statistical analysis plan (SAP), not in a software default.

Take a longitudinal prevention trial. A participant attends a protocol-mandated visit at month 12 and provides blood for a central laboratory assay; the result is negative. At the month 15 visit the assay is repeated and is positive. The participant has had no symptoms. What does the clinical database actually hold? Not an infection date or a biological transition moment—only two visit transactions separated by roughly three months of unobserved time.

In survival analysis this is interval censoring. Introductory tutorials often define interval and left censoring and then set them aside; one British Journal of Cancer tutorial series (Clark et al., 2003) states that it will consider right-censored data only. Periodically assessed outcomes, however, generate four observation patterns:

• Exact event time (L = R): The event date is known. In a scheduled-screening trial this is uncommon; it usually requires an unscheduled diagnostic test that pins the event to a specific day.

• Interval-censored record (0 < L < R < ∞): The event occurred after the last negative assessment L and at or before the first positive assessment R; all that is known is L < T ≤ R.

• Left-censored record (L = 0, R < ∞): The event is detected at the first post-baseline assessment. Provided baseline infection has been ruled out (see the callout below), it occurred between baseline (time 0) and R.

• Right-censored record (0 < L < ∞, R = ∞): The participant completes follow-up, withdraws, or is censored for another reason without ever testing positive. All that is known is T > L, where L is the final negative assessment.

To see how ordinary this mixed structure is, look at the Bangkok injecting-drug-user cohort that StataCorp uses to demonstrate its interval-censored Cox command, stintcox. The 1,124 subjects initially tested HIV-negative and were then tested approximately every four months; the exact infection time was never observed, only the interval between blood tests, stored as lower and upper endpoint variables. Stata's fitted output classifies the records as:

• 41 left-censored records: an upper bound is known, but no earlier negative follow-up test bounds the event from below.

• 92 interval-censored records: a negative test followed by a positive test.

• 991 right-censored records: never observed positive; the event time is known only to exceed the last negative test.

• 0 exact event times: not one record has an observed infection date.

The lesson for clinical operations and statistical programming: whenever an endpoint can only be detected at scheduled laboratory tests, imaging, endoscopy, or cognitive assessments, records without exact event times are expected. They are not a data defect; they are what the observation process produces.

Clinical database tables do not naturally output paired L and R values. Instead, electronic data capture (EDC) systems store a fragmented transaction log: visit dates, lab sample collection timestamps, specimen receipt dates, assay results, out-of-window re-tests, and query resolutions. Transforming this raw operational visit trail into rigorous biostatistical variables requires explicit derivation rules locked in the dataset specification:

1. Derivation of L (Lower Bound): Defined as the elapsed time (e.g. days from randomization or first investigational dose) to the latest valid clinical assessment at which the protocol-defined diagnostic test was unequivocally negative. For left-censored records where no post-baseline negative test exists, L is set to 0 (baseline).

2. Derivation of R (Upper Bound): Defined as the elapsed time to the earliest valid clinical assessment at which the diagnostic test satisfied all protocol-specified confirmation criteria for the endpoint. For right-censored records where no positive result occurs during study participation, R is coded as infinity (or a designated software sentinel such as a missing value depending on software requirements).

While this derivation appears straightforward in theory, real clinical trials introduce operational friction that directly challenges variable integrity. Trial programmers must implement robust QC algorithms to address three critical scenarios:

• Missed and skipped visits: A participant tests negative at month 3, misses the month 6 assessment, and tests positive at month 9. The honest interval is (month 3, month 9]. Data management must never assume the event occurred at month 6 or impute a negative result for the missed visit. The missed visit legitimately widens the window, and the analysis must carry that extra uncertainty.

• Out-of-window visits: Protocols allow assessment windows—for example, a nominal 12-week visit with a ±14-day window, so the same "month 3" visit can fall on day 72 for one participant and day 97 for another. Derive L and R from actual days elapsed since the time origin, never from nominal visit numbers. Converting nominal visits into fixed days (for example, visit number × 90) discards real timing variation and adds rounding artifacts to the likelihood.

• Discordant and confirmatory test algorithms: Many diagnostic algorithms require reflex or second-specimen confirmation after a reactive screen. If a reactive result on day 90 needs a confirmatory test on a later specimen (say day 105), the protocol must prespecify whether R is the date of the first reactive specimen that is subsequently confirmed or the confirmation date. Anchoring R to the earliest specimen later confirmed positive is one defensible choice; whichever rule is chosen should be written down before unblinding and applied identically in both arms.

Faced with interval-censored data, clinical study teams frequently resort to two computational shortcuts inherited from legacy right-censored software workflows:

1. Right-point imputation (detection date): Assigning the date of the first positive assessment R as the exact time of the event (T = R).

2. Midpoint imputation: Setting the event time to the exact arithmetic center of the observation window, T = (L + R) / 2.

Both shortcuts are documented as problematic. Eaton (2024, Clinical Trials) reviews the first-detection approach for composite endpoints that include an interval-censored nonfatal event, and the SAS Global Forum paper by So, Johnston, and Kim (2010) summarizes literature showing that conventional midpoint and right imputation are biased and less efficient than interval-aware methods, especially when assessment is infrequent or imbalanced. Three consequences matter most for trial teams:

1. Upward bias in Kaplan-Meier curves. Assigning the first positive date R assumes the participant stayed event-free until the day of the visit. Eaton notes that under this naive approach the Kaplan-Meier estimator is biased upward, particularly between planned visit times, and that curves often show large drops near assessment times—reflecting when events were detected rather than when they occurred. Midpoint imputation moves events earlier, but it still places them at artificial times dictated by the visit schedule rather than by the underlying event process.

2. Hazard-ratio bias when assessment schedules differ by arm. Visit frequency is not always identical across arms. In a hypothetical example, one regimen requires monthly in-clinic injections while the comparator is a daily oral product reviewed quarterly; different adverse-event profiles can also trigger extra unscheduled testing in one arm.

For composite endpoints with an interval-censored component, Eaton cautions that when assessments are more frequent in one treatment arm, the naive hazard-ratio estimator can be substantially biased—which is why trials conventionally use the same assessment schedule in both arms—and that bias in both the naive Kaplan-Meier estimator and the naive hazard ratio increases as visit frequency decreases. The mechanism is intuitive: the more frequently assessed arm detects asymptomatic events sooner, so its recorded event times shift earlier even when the true event process is identical. The counterpoint matters as well. With a common schedule, Eaton summarizes one analysis in which the naive Cox hazard ratio was biased toward the null in the scenarios considered and several simulation studies that judged its bias generally low; she also notes that the naive right-censored approach is very prevalent and is endorsed by FDA for progression-free survival. The case against naive analysis is therefore strongest for survival-curve estimates, infrequent assessments, and unequal schedules.

3. Miscalibrated uncertainty. When an imputed date is fed into Kaplan-Meier or Cox software, the software treats it as an observed time; the width of each (L, R] window never enters the variance. The bias also compounds in summary measures: Eaton reports that when the area under a naive Kaplan-Meier curve was used to estimate restricted mean time alive and event-free, the bias accumulated across the curve, and in one simulation study the coverage probability of that estimate dropped as low as 14%.

None of this means a midpoint is never acceptable. The defensible uses are specific, and the boundary depends on what the analysis is estimating.

Prinja, Gupta, and Verma (2010) state the permissive position plainly: if the periodicity of examination is at a justified frequency, interval-censored data can be dealt with as point censored. The same review also acknowledges that imputation techniques are "laden with problems." Whether the shortcut is defensible today depends on the estimand and the purpose of the analysis:

• Person-time incidence-rate estimands: In HIV pre-exposure prophylaxis trials covered by FDA's March 2019 guidance, the primary endpoint is not a survival curve or a hazard ratio; it is the HIV infection rate per 100 person-years, analyzed in the intent-to-treat population. In a rate, events are the numerator and person-time is the denominator. Dating an infection at the midpoint instead of the first positive test removes half of that participant's (L, R] interval from the person-time at risk, so the choice affects only the denominator and its effect can be bounded and reported. It is still an imputed value, not an observed date.

• Current registered practice: The LAPIS trial statistical analysis plan (dated 21 May 2026, NCT06250504)—a cluster-randomised effectiveness and implementation trial in which HIV incidence is a secondary outcome reported per 100 person-years—states: "Date of HIV infection will be estimated as the midpoint between the last negative and first positive HIV tests." Participants lost to follow-up are censored at their last HIV-negative test. Its missing-data section adds that event times will not be imputed for time-to-event outcomes: participants with no follow-up HIV test are censored at their last observed negative test. In other words, the midpoint dates observed seroconversions inside a rate outcome; it is not used to create outcomes for participants who were never retested.

• Bounded estimation in HIV research and surveillance (CEPHIA / EDDI): Pilcher et al. (2019) describe an estimated date of detectable infection (EDDI) bounded by earliest- and latest-plausible dates inferred from each assay's diagnostic delay and the person's testing history. The best single estimate is the midpoint of that plausible interval, but the interval is retained with it, and information from additional test encounters can narrow it. The context is research, surveillance, recency estimation, and clinical management—not confirmatory trial endpoint analysis.

The working rule: a midpoint can be defended as prespecified bookkeeping for person-time denominators or as a point estimate within bounded estimation, provided the original bounds remain retrievable. It is hard to defend as an undocumented shortcut that pushes interval data into right-censored confirmatory survival analyses.

Established methods analyze the (L, R] record directly, without inventing a date. Four elements matter when planning an interval-censored endpoint:

1. The Turnbull nonparametric maximum likelihood estimator (NPMLE). Peto (1973) and Turnbull (1976) showed that the NPMLE of the survival function for interval-censored data can decrease only on a set of nonoverlapping intervals, often called Turnbull intervals; Turnbull's self-consistency (EM) algorithm computes it. It generalizes the Kaplan-Meier estimator to any mix of interval-, left-, and right-censored records. Within each Turnbull interval the estimator assigns probability mass without specifying how it is distributed, so the curve is not uniquely determined there—state that explicitly in figures and tables.

2. Interval-censored proportional hazards models. Finkelstein (1986) proposed a proportional hazards model for interval-censored data. Instead of a partial likelihood evaluated at exact failure times, each participant contributes the probability that the event fell inside the observed window: L(β) = ∏ [ S(L_i | x_i) − S(R_i | x_i) ]. Software routes documented in the vendor sources cited here include:

• SAS: So, Johnston, and Kim (2010) describe SAS macros for the NPMLE (%EMICM) and for generalized log-rank tests (%ICSTEST and %ICE), and note that the LIFEREG procedure (SAS/STAT) and the RELIABILITY procedure (SAS/QC) fit parametric models such as the Weibull and lognormal to interval-censored data and also provide the NPMLE. Newer SAS/STAT releases may offer dedicated interval-censored procedures; confirm names, versions, and validation status in current vendor documentation before writing them into an SAP.

• Stata: stintcox fits a semiparametric Cox model to interval-censored data in single-record (lower and upper endpoint) or multiple-record (examination time plus event status) format. StataCorp contrasts it with older "semiparametric" approaches that relied on spline or piecewise-exponential baseline hazards, and documents proportional-hazards checks tailored to interval-censored Cox models.

• Open-source routes: Open-source packages for interval-censored estimation and regression also exist. None is covered by the sources cited here, so verify package versions, methods, and qualification under your validation procedures before naming one in an SAP.

3. Generalized log-rank tests for interval data. The ordinary log-rank test needs exact event times to rank. Generalized log-rank tests compare survival functions directly from interval-censored records: Zhao and Sun (2004) extended the approach to data that also contain exact failure times and estimate its variance by imputation, while the Sun, Zhao, and Zhao (2005) family includes Finkelstein's (1986) score test as a special case.

4. Power planned for the observation process, not for exact times. Conventional Cox sample-size calculations assume events are observed exactly. Eaton's review reports a simulation in which a design sized for 90% power under that assumption achieved only 81–89% empirical power with the naive hazard-ratio estimator when the nonfatal event was assessed intermittently; a parametric estimator designed for this censoring recovered some of the loss (85–90%), and the gap narrowed as assessments became more frequent. Interval-aware methods are not free either: they are more complex to apply, generally perform best when visits are reasonably dense, and require a non-informative visit process. Build the planned assessment interval and expected interval width into the sample-size discussion during protocol development.

Because a hazard ratio is difficult to interpret under non-proportional hazards, Eaton also points to the difference in restricted mean time alive and event-free up to a chosen restriction time—an effect measure whose interpretation is not tied to proportional hazards, obtained as the area under an appropriately estimated event-free survival curve. Computed from a naive Kaplan-Meier curve, it inherits that curve's bias. For choosing and justifying the horizon, see our guide to restricted mean survival time.

To make this concrete for programming and data-management teams, the synthetic ledger below follows five participant trajectories—covering interval-censored, left-censored, and right-censored records—through three approaches: naive detection-date entry, midpoint imputation, and interval-aware analysis.

flowchart TD
  subgraph RawVisitData [Visit trail]
    V1["Visit 1: negative result"]
    V2["Visit 2: missed, no result"]
    V3["Visit 3: confirmed positive result"]
  end
  subgraph DatasetDerivation [Analysis dataset]
    L["L: days to last negative assessment"]
    R["R: days to first positive assessment"]
  end
  subgraph AnalysisRouting [Analysis input]
    B1["Naive: event time set to R"]
    B2["Midpoint: event time set to (L + R) / 2"]
    B3["Interval-aware: keeps the (L, R] pair"]
  end
  V1 --> L
  V2 -.->|widens the interval| R
  V3 --> R
  L --> B1
  R --> B1
  L --> B2
  R --> B2
  L --> B3
  R --> B3

The ledger shows where the approaches diverge. For SUBJ-102, who missed the month 6 visit, midpoint imputation assigns day 178.5—asserting an event in the middle of a six-month gap in which nothing was observed—while the interval-aware input keeps the wide (89, 268] window and lets the likelihood spread probability across it. For SUBJ-103, the naive analysis records an event on day 28 and the midpoint analysis on day 14, whereas the interval-aware input says only that the event occurred within the first 28 days. For SUBJ-104 and SUBJ-105, all three approaches receive the same right-censored record, at day 365 and day 92 respectively: the shortcuts change only how observed events are dated.

Under ICH E9(R1), the variable (endpoint) is an estimand attribute that must be precisely specified alongside the treatment, the population, the handling of intercurrent events, and the population-level summary (see our guide to specifying intercurrent events). E9(R1) does not mention interval censoring, so treating interval handling as part of the variable specification is our interpretation; it follows from that requirement and from the addendum's expectation that sensitivity analyses explore the robustness of conclusions to departures from the main analysis's assumptions.

To prevent methodological disputes at unblinding, the SAP should lock the following specifications:

1. Definition of L and R: the time origin and scale (for example, integer days from randomization), the assays that qualify as negative and positive, the rule that sets R when confirmation is required, and the rule for inconclusive or unconfirmed preliminary results.

2. Rules for missed and out-of-window visits: state that a missed visit widens (L, R] to the nearest valid adjacent assessments, that no intermediate negative result will be imputed, and that actual assessment dates, not nominal visit numbers, define the bounds.

3. Primary versus sensitivity estimators: if an interval-aware analysis is primary, prespecify the estimator, software and version, the baseline-hazard approach (for example, a semiparametric Cox model versus spline or piecewise-exponential baselines), and the generalized log-rank test. If a midpoint-imputed rate or survival analysis is primary, prespecify an interval-aware analysis of the same estimand as a sensitivity analysis.

4. Extreme-bound sensitivity analyses: as a stress test, analyze the placement most favourable to the experimental arm (T = R in that arm and T = L in the control arm) and the reverse placement. If conclusions hold under both, placement of events within their intervals cannot explain the result. Left-censored records use L = 0.

5. Monitoring of assessment-schedule balance: prespecify a check of visit-interval lengths and missed-visit proportions—pooled during blinded data review, and by arm through the independent data monitoring committee or at database lock—as an early signal of differential surveillance.

When an interval-censored endpoint reaches the clinical study report and the submission, reviewers can judge the analysis only if the observation process is visible alongside the summary effect estimate.

Three diagnostic summaries make it visible:

• Distribution of interval widths (R − L): report the median, interquartile range, and 90th percentile of window widths among participants with the endpoint, by treatment arm. Imbalanced widths may indicate differential follow-up intensity.

• Observation-pattern counts: tabulate the number and proportion of left-censored, interval-censored, and right-censored participants in each arm, and any baseline infections excluded under the screening rules.

• Evidence on the visit process: interval-censored likelihood methods assume a non-informative visit process. If participants attend early or request unscheduled tests because they suspect the event, the observation process becomes informative. Document whether unscheduled visits contributed to positive-test capture and assess the impact with sensitivity analyses.

Limitations. Interval-aware methods have boundaries of their own. The Turnbull NPMLE is not uniquely defined inside its intervals. Likelihood-based methods require a non-informative visit process and perform best when visits are reasonably dense; informative missed visits need explicit justification and sensitivity analysis, which this article can frame but not resolve. Eaton's quantitative findings come from composite endpoints of death plus an interval-censored nonfatal event, for which approaches such as the Frydman–Szarek NPMLE, multi-state parametric models, and sieve and kernel estimators are designed; magnitudes may not transfer to every endpoint. The SAS and Stata sources are vendor documentation, not independent evidence of estimator performance, and software capabilities change between versions. The ledger above is synthetic.

For related guidance, see Time-to-Event Endpoints: Writing Censoring Rules Readers Can Follow, Statistical Analysis Plans for Endpoints: What Must Be Locked Before Unblinding, Clinical Trial Assessment Windows: Recording a Late Visit Without Backdating, and Missing Data vs Intercurrent Events: Estimand-Aligned Sensitivity Analysis.