Study of Ibrutinib Combined With Venetoclax in Subjects With Mantle Cell Lymphoma (MCL): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Ibrutinib Combined With Venetoclax in Subjects With Mantle Cell Lymphoma (MCL) (NCT03112174), a randomized phase 3 study. The primary outcome is Number of Participants With Tumor Lysis Syndrome (TLS) Events (Safety Run-in).

2. Clinical Question

3. Trial Design

NCT03112174 is a completed Phase 3 study of ibrutinib in combination with venetoclax in people with mantle-cell lymphoma. The registry describes a multinational, randomized, double-blind study comparing ibrutinib plus venetoclax with ibrutinib plus placebo. It lists a parallel design, triple masking, and enrollment of 366. The registry record does not report the specific masking roles.

The record also describes groups beyond the randomized comparison. The safety run-in included participants with low or high baseline TLS risk and used open-label concurrent ibrutinib and venetoclax. A treatment-naive open-label arm used ibrutinib and venetoclax with a 5-week venetoclax ramp-up schedule. Outcomes from these groups should not be treated as randomized comparisons with one another.

In the randomized phase, assigned venetoclax or placebo was planned for approximately 104 weeks. After that, participants were to continue ibrutinib monotherapy until disease progression, unacceptable toxicity, or withdrawal of consent. The assigned venetoclax or placebo was to stop after 104 weeks regardless of response assessment.

The study began on 2017-06-19, had primary completion on 2024-06-26, and is listed as completed. The registry lists overall response, complete response, minimal residual disease-negative remission, and overall survival among secondary outcomes. The registry record does not report the protocol’s sample-size justification or detailed statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All treated safety run-in participants

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Tumor Lysis Syndrome (TLS) Events (Safety Run-in), measured over After at least 3 months of treatment, with an overall median treatment duration of 20.0 months.

The primary endpoint counts participants in the safety run-in who had a tumor lysis syndrome event. The registry defines laboratory TLS using Howard criteria and requires that it not resolve within 72 hours despite protocol-required management. Clinical TLS also uses Howard criteria, with specific exceptions for this safety run-in assessment. For the run-in, a serum creatinine increase must be greater than 1.0 mg/dL from pretreatment baseline to count as clinical TLS. For participants with baseline renal dysfunction, defined as creatinine clearance less than 60 mL/min, clinical TLS requires laboratory TLS plus seizures, cardiac dysrhythmia, or death.

A count is useful for reporting whether an event occurred in a safety-focused group, particularly when the endpoint is a defined adverse clinical or laboratory event. Here, the registry gives the count and the number of participants in each baseline-risk group. It does not report a formal comparative estimate or confidence interval for this primary endpoint. The stated timeframe is after at least 3 months of treatment, with an overall median treatment duration of 20.0 months.

Because the primary endpoint is an event count in a safety run-in, it answers a different question from the randomized phase’s comparative efficacy outcomes. It does not estimate a randomized treatment effect, and the two risk groups should not be interpreted as if they had been randomly assigned to different treatments.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Statistical methods help distinguish what the registry directly reports from what can reasonably be inferred. The primary endpoint is a count of participants with TLS events. It is not a percentage comparison or a randomized contrast. The registry reports one event in the increased-risk group and none in the low-risk group, but no comparative test or interval estimate for this endpoint. General statistical point: when event counts are small, the observed counts can be highly sensitive to individual events, so they should be read descriptively and with attention to the size and structure of the groups.

What does a confidence interval describe?

General explanation: a confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. It describes statistical uncertainty in an estimate; it is not a range containing a specified proportion of individual participant outcomes, and it does not account automatically for biases or unmeasured differences. The registry reports 95% confidence intervals for the randomized secondary outcomes. For a rate ratio, the no-difference reference is 1. For a hazard ratio, the no-difference reference is also 1. If the interval includes 1, the interval does not rule out that reference value at the stated confidence level.

The registry also reports confidence intervals for arm-specific response percentages. Those intervals describe uncertainty around each arm’s response estimate. Overlap or non-overlap of two separate arm-specific intervals is not a substitute for the direct comparative analysis, which uses its own estimate and interval.

How should the randomized response comparisons be read?

The complete-response analysis is reported as a Cochran-Mantel-Haenszel rate ratio. The registry reports a rate ratio of 1.658, with a 95% confidence interval from 1.240 to 2.218. The interval lies above 1. The overall-response randomized comparison is also reported using a Cochran-Mantel-Haenszel rate ratio: 1.101, with a 95% confidence interval from 0.973 to 1.247. That interval includes 1. The registry’s reported analyses should take precedence over simple unadjusted recalculations when the two differ; the record does not flag a discrepancy for these analyses.

The posted unadjusted calculations are not the same as the registry’s reported analyses. They use summary counts and do not reproduce all features of a sponsor analysis. They can be useful as a statistical cross-check, but they are not a replacement for the trial’s reported analysis. In general, adjustment or stratification can alter an estimate or its uncertainty, depending on the analysis design and data structure.

What does the survival analysis estimate?

Overall survival is a time-to-event outcome. General explanation: survival analysis uses the time until an event and can account for participants whose event has not occurred by the end of available follow-up, provided the analysis handles those observations as censored. The registry reports a log-rank analysis and a hazard ratio of 0.832, with a 95% confidence interval from 0.602 to 1.151. The interval includes 1. The record does not report enough detail to assess the censoring rules or other modeling assumptions.

A hazard ratio compares event rates over follow-up under the assumptions of the analysis; it is not a ratio of median survival times. The reported medians provide another summary of the survival distributions. One median is not estimable for the treatment-naive open-label arm, and the registry reports only a lower confidence limit for that estimate. A missing upper limit is not evidence that survival is unlimited; it means that limit is not reported in the registry record.

What do the sample-size illustrations mean?

General explanation: a sample-size calculation is a planning exercise that estimates how many participants or events would be needed under stated assumptions to detect a specified effect with a chosen power and significance level. The registry’s illustrations are computed from the observed effect, with a two-sided significance level of 0.05, equal allocation for two-arm comparisons, and a normal approximation. The displayed rows consider planning for 100%, 75%, and 50% of the observed effect. For time-to-event outcomes, the illustrations count total events; for other outcomes, they give participants per arm.

These figures are not the trial’s original design justification and do not measure the study’s observed power. The registry record does not report the original sample-size justification. Planning estimates based on an observed effect are especially dependent on that effect estimate, which is itself uncertain. They should therefore be read as conditional illustrations, not as evidence that the study was or was not adequately powered.

General explanation: over-dispersion occurs when outcome variability exceeds what a statistical model assumes. It can make standard errors too small and confidence intervals too narrow if the model does not account for the extra variability. The primary outcome is a count in small safety groups, but the registry does not report a count-model analysis or a dispersion assessment. No conclusion about over-dispersion can be drawn from the record.

10. Exact Estimates for Each Arm

No two-arm comparison is shown for this trial, but each arm's result can still be summarized with exact interval estimates computed from the posted counts. The Clopper-Pearson interval is exact and conservative; the Wilson interval is a common closer-to-nominal alternative; the Bayesian credible interval uses a uniform Beta(1, 1) prior. For small groups the three can differ noticeably.

R code and output

arm    <- c("Safety Run-in: Increased TLS Risk at Baseline", "Safety Run-in: Low TLS Risk at Baseline")
n      <- c(15, 6)
events <- c(1, 0)
for (i in seq_along(n)) {
  ci <- binom.test(events[i], n[i])$conf.int          # Clopper-Pearson exact interval
  cr <- qbeta(c(0.025, 0.975), 1 + events[i], 1 + n[i] - events[i])   # Bayesian, uniform Beta(1,1) prior
  wi <- (function(x, n) { p <- x / n; z <- qnorm(0.975); d <- 1 + z^2 / n
    c((p + z^2 / (2 * n) - z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d, (p + z^2 / (2 * n) + z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d) })(events[i], n[i])
  cat(sprintf("ARM|%s|%d|%d|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f\n", arm[i], n[i], events[i], 100 * events[i] / n[i],
              100 * ci[1], 100 * ci[2], 100 * wi[1], 100 * wi[2], 100 * cr[1], 100 * cr[2]))
}

ARM  Safety Run-in: Increased TLS Risk at Baseline  15  1  6.7  0.2  31.9  1.2  29.8  1.6  30.2
ARM  Safety Run-in: Low TLS Risk at Baseline  6  0  0.0  0.0  45.9  0.0  39.0  0.4  41.0

11. Multiplicity, Missing Data and Analysis Populations

The registry record lists many outcomes and reports several secondary analyses, but it does not report a multiplicity adjustment, a testing hierarchy, or which secondary outcomes were designated confirmatory. When multiple hypotheses are tested, the probability of at least one chance finding can rise. General statistical explanation: procedures such as adjusted significance thresholds or a prespecified sequence of tests can help control that risk. Without a reported approach, the secondary p-values should not be treated as if each were the sole planned test.

The record does not report how missing outcome data were handled, how many participants were missing each outcome, or whether sensitivity analyses addressed missingness. It also does not report detailed analysis-population definitions, such as the exact membership rules for the primary or secondary analyses. These omissions matter because exclusions and missing observations can affect both the estimate and how broadly it applies.

The registry reports analysis group sizes for the displayed outcomes, but those counts alone do not establish the full analysis population or explain any differences between randomized enrollment and outcome denominators. The record does not report detailed rules for censoring in the survival analysis, nor does it provide enough information to evaluate the assumptions behind handling incomplete follow-up.

These limitations do not demonstrate that the analyses were conducted incorrectly. They identify details that cannot be assessed from the registry record. The most defensible reading is to distinguish the explicitly reported randomized analyses from descriptive open-label findings and to avoid treating unadjusted secondary results as definitive when the multiplicity and missing-data procedures are not reported.

12. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyrexia (20.0%), pancytopenia (16.7%), retroperitoneal haemorrhage (16.7%), cellulitis (16.7%), staphylococcal bacteraemia (16.7%).

The primary safety endpoint is a TLS event count within the safety run-in: one event among 15 participants at increased baseline TLS risk and none among 6 at low baseline risk. The registry also reports serious adverse events and deaths by study group. In the increased-risk run-in group, 15 participants were at risk for serious adverse events and 15 were reported as affected; 8 deaths are listed. In the low-risk run-in group, 3 of 6 were reported as affected by serious adverse events, and 3 deaths are listed.

For the randomized ibrutinib-plus-venetoclax group, 92 of 134 participants were reported as affected by serious adverse events and 70 deaths are listed; for the ibrutinib-plus-placebo group, the corresponding counts are 86 of 132 and 78. In the treatment-naive open-label arm, 48 of 78 were reported as affected by serious adverse events and 20 deaths are listed. These counts are descriptive, and the registry record does not provide an adjusted comparison of serious adverse event risk or deaths in this summary.

The listed serious event terms include pyrexia at 20.0%, and pancytopenia, retroperitoneal haemorrhage, cellulitis, staphylococcal bacteraemia, and accidental overdose each at 16.7%. These term percentages should be interpreted using the registry’s adverse-event reporting context; they are not treatment-effect estimates. Differences in group size, follow-up, and study phase mean the counts should not be compared as if they were a single randomized safety contrast.

13. What the Result Does, and Does Not, Mean

The registry results describe several distinct questions. The primary endpoint records TLS events during the safety run-in, with one event in the increased-risk group and none in the low-risk group. The randomized phase compares ibrutinib plus venetoclax with ibrutinib plus placebo on response and survival outcomes. The treatment-naive open-label arm provides a separate set of observations. Keeping these populations and purposes distinct is essential to interpreting the record.

For the randomized phase, the complete-response analysis reports a rate ratio whose confidence interval is above 1, while the overall-response and overall-survival comparison intervals include 1. These findings express different amounts and types of statistical evidence for different endpoints. They do not establish that every participant experienced the average outcome, and they do not resolve uncertainty beyond what the reported estimates and intervals express.

The record does not support a causal comparison between the treatment-naive open-label arm and randomized groups. Nor does a count of rare events in small run-in groups establish that an event is impossible in a risk category. A lack of a reported statistically distinguishable difference is not proof that two treatments are equivalent; equivalence or noninferiority requires an appropriate design and analysis, details of which are not reported for such a claim.

These results are not medical advice and do not determine what treatment is appropriate for an individual. They describe the registry’s posted outcome summaries and the uncertainty attached to selected estimates. The record does not report enough detail to resolve every question about the analysis plan, missing data, multiplicity, or outcome ascertainment. Conclusions should therefore remain limited to the endpoint, population, and comparison actually reported.

14. Why This Trial Matters Statistically

This trial illustrates why biostatistical interpretation starts by identifying the question each endpoint answers. A safety event count from a run-in is not the same estimand as a randomized efficacy comparison. Treating them as interchangeable would obscure both the limited size of the run-in groups and the role of randomization in the later phase.

It also demonstrates why a point estimate is not the whole result. The complete-response rate ratio is accompanied by an interval that lies above 1, while the overall-response rate ratio and survival hazard ratio have intervals that include 1. The confidence intervals make the differing precision and compatibility with a no-difference value visible. Reporting uncertainty prevents an estimate from being read as an exact or universally applicable effect.

Finally, the registry includes an open-label treatment-naive arm alongside the randomized comparison. Statistical interpretation must respect that design distinction: randomization supports a direct comparison of the randomized groups, while an open-label arm cannot be assumed exchangeable with them. The record also highlights the importance of transparency about multiplicity, analysis populations, missing data, and planning assumptions. Without those details, readers can interpret the posted estimates but cannot fully audit every aspect of the analysis.

The broad lesson is methodological rather than promotional: match each conclusion to its population, endpoint, comparison, and uncertainty. That discipline keeps descriptive safety findings from being overstated and prevents secondary outcomes from carrying more confirmatory weight than the registry record warrants.

15. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is reported for small safety run-in groups and as counts without a confidence interval or formal comparison. The groups are organized by baseline TLS risk, not by randomized treatment assignment. The registry record does not report a comparative estimate for this primary outcome, so the group counts should not be used to infer a treatment effect or a reliable difference between risk categories.

The study includes distinct populations and phases, including an open-label treatment-naive arm and the randomized phase. Comparisons involving the open-label arm are descriptive rather than randomized. Follow-up contexts also differ: the randomized outcomes are described for an overall median time on study of 61.34 months, while the treatment-naive arm’s overall median time on study is 40.51 months for outcomes where both contexts are reported. These differences limit direct comparison across arms.

Some estimates have incomplete interval limits. For the randomized combination arm’s median overall survival, the registry reports 44.9 months with a lower confidence limit of 31.9 months but no upper limit. For the treatment-naive open-label arm, the median is not estimable; the record gives a lower confidence limit of 44.2 months and no upper limit. These should not be filled in by inference.

The registry record does not report detailed missing-data methods, analysis-population definitions, multiplicity handling, censoring rules, or the trial’s original sample-size justification. The planning illustrations are based on observed effects and are not the original design calculations. These gaps limit independent assessment of the robustness and confirmatory status of the posted outcomes.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Study of Ibrutinib Combined With Venetoclax in Subjects With Mantle Cell Lymphoma (MCL) — NCT03112174.
• Registry record last updated 2025-07-22; status last verified 2025-07.
• Results first posted 2025-07-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

19. Record Summary

NCT03112174 is a completed Phase 3, randomized, parallel, triple-masked study of ibrutinib with venetoclax versus ibrutinib with placebo in mantle-cell lymphoma. The record lists enrollment of 366 and also describes a safety run-in and treatment-naive open-label arm.

The primary outcome counts TLS events in treated safety run-in participants. The registry reports one event among 15 participants at increased baseline TLS risk and none among 6 participants at low baseline risk. Secondary randomized findings include a complete-response rate ratio of 1.658, an overall-response rate ratio of 1.101, and an overall-survival hazard ratio of 0.832, each with its reported confidence interval. The randomized overall-response and overall-survival intervals include 1; the complete-response interval does not.

The registry record does not report several details needed for a full audit of the analyses, including missing-data procedures and multiplicity handling. Open-label findings should be kept distinct from randomized comparisons.