A Phase Ib/II Study Investigating the Safety, Tolerability, Pharmacokinetics, and Efficacy of Mosunetuzumab (BTCT4465A) in Combination With CHOP or CHP-Polatuzumab Vedotin in Participants With B-Cell Non-Hodgkin Lymphoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase Ib/II Study Investigating the Safety, Tolerability, Pharmacokinetics, and Efficacy of Mosunetuzumab (BTCT4465A) in Combination With CHOP or CHP-Polatuzumab Vedotin in Participants With B-Cell Non-Hodgkin Lymphoma (NCT03677141), a randomized phase 1, phase 2 study. The primary outcome is Complete Response (CR) Rate at the Time of Primary Response Assessment (PRA) Based on Positron Emission Tomography - Computed Tomography (PET-CT) as Determined by Independent Review Committee (IRC).

2. Clinical Question

3. Trial Design

This was a Phase Ib/II, randomized, controlled, open-label, multicenter study with a parallel-group model. The registry lists 117 participants enrolled overall and a completed status. The study start is recorded as 2019-03-08 and primary completion as 2023-10-12. The design included dose-finding groups in Phase Ib and several Phase II cohorts, so the total enrollment is not the number contributing to the primary randomized comparison.

The main randomized Phase II contrast was Arm 1, mosunetuzumab plus CHP-polatuzumab vedotin, versus Arm 2, rituximab plus CHP-polatuzumab vedotin. Participants were grouped according to the treatment arm assigned at randomization for the primary efficacy analysis. The endpoint record lists 40.0 participants for Arm 1 and 22.0 for Arm 2. Group C, a Phase II mosunetuzumab plus CHOP cohort, was included in secondary analyses. A separate Phase II M-CHOP 1L DLBCL arm is described, but the registry says no participants were enrolled to that arm.

The study was unmasked: participants and study personnel were not assigned to blinded treatment groups according to the registry. Randomization can support a fair comparison of assigned groups, while lack of masking can affect behavior, care, or judgments in some settings. For the primary endpoint, review was by an independent review committee, which distinguishes the assessment process from investigator-determined secondary response outcomes. The registry record does not report the randomization procedure, allocation ratio as planned, stratification factors, or details of how the independent committee operated.

The study evaluated safety, tolerability, pharmacokinetics, and efficacy. Its stated scope includes mosunetuzumab with CHOP and, subsequently, mosunetuzumab with CHP-polatuzumab vedotin, in addition to the randomized rituximab comparison. It therefore combines dose-finding and efficacy components rather than representing a single two-arm efficacy trial throughout. The protocol's original sample-size rationale and other design assumptions are not reported in the registry record.

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: The intent-to-treat (ITT) population consisted of all participants. Efficacy analyses for Arms A1, A2, and B were exploratory. The primary efficacy analysis compared Arm 1 vs Arm 2, with participants grouped according to the treatment arm assigned at randomization. Group C was included in secondary efficacy analysis, and efficacy analyses for Arms A1, A2, and B were exploratory.

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Complete Response (CR) Rate at the Time of Primary Response Assessment (PRA) Based on Positron Emission Tomography - Computed Tomography (PET-CT) as Determined by Independent Review Committee (IRC), measured over 6-8 weeks after either C6D1 or last dose of study treatment.

The primary endpoint was the percentage of participants with complete response at the time of primary response assessment. The registry defines complete response using the Lugano 2014 Response Criteria and specifies PET-CT as the basis for assessment by an independent review committee. Assessment was scheduled 6-8 weeks after either C6D1 or the last dose of study treatment. The endpoint is a binary response outcome: each participant is classified as having or not having a complete response for this measure, and the reported rate is the proportion classified as complete response.

Complete response is used as an efficacy measure because it records whether the predefined assessment indicates that the criteria for complete response have been met. It is not a direct measure of how long a response lasts, how a participant feels, or what happens after the assessment. The registry lists duration of response, progression-free survival, event-free survival, and other response outcomes separately, reflecting that these capture different aspects of disease course and response.

For the primary comparison, the registry reports a complete response rate of 72.5% among 40.0 participants in Arm 1 and 77.3% among 22.0 participants in Arm 2. The confidence intervals are wide enough that the observed percentages should be read with their uncertainty in mind. In general, an endpoint can be useful for comparing groups without answering every clinically relevant question; its interpretation depends on the assessment criteria, timing, analysis population, and precision of the estimates.

7. Results Posted in the Registry

• Arm 2: Phase II Rituximab + CHP-Pola (Randomized): 77.3% (17/22) versus 72.5% (29/40) on control; risk difference 4.8 percentage points (95% CI -17.5 to 27.1), risk ratio 1.07 (0.79–1.43); unadjusted two-proportion z-test p = 0.681.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

CR Rate at PRA Based on CT Only as Determined by the Investigator (Phase II)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized): 47.5% (19/40) versus 50.0% (20/40) on control; risk difference -2.5 percentage points (95% CI -24.4 to 19.4), risk ratio 0.95 (0.61–1.49); unadjusted two-proportion z-test p = 0.823.
  • Arm 2: Phase II Rituximab + CHP-Pola (Randomized): 31.8% (7/22) versus 50.0% (20/40) on control; risk difference -18.2 percentage points (95% CI -43.1 to 6.7), risk ratio 0.64 (0.32–1.26); unadjusted two-proportion z-test p = 0.167.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2: Phase II Rituximab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.

Overall Response Rate (ORR) at PRA Based on PET-CT as Determined by the Investigator (Phase II)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized): 80.0% (32/40) versus 87.5% (35/40) on control; risk difference -7.5 percentage points (95% CI -23.6 to 8.6), risk ratio 0.91 (0.75–1.11); unadjusted two-proportion z-test p = 0.363.
  • Arm 2: Phase II Rituximab + CHP-Pola (Randomized): 77.3% (17/22) versus 87.5% (35/40) on control; risk difference -10.2 percentage points (95% CI -30.5 to 10.1), risk ratio 0.88 (0.68–1.14); unadjusted two-proportion z-test p = 0.295.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2: Phase II Rituximab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.

ORR at PRA Based on CT Only as Determined by the Investigator (Phase II)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized): 72.5% (29/40) versus 85.0% (34/40) on control; risk difference -12.5 percentage points (95% CI -30.2 to 5.2), risk ratio 0.85 (0.68–1.07); unadjusted two-proportion z-test p = 0.172.
  • Arm 2: Phase II Rituximab + CHP-Pola (Randomized): 81.8% (18/22) versus 85.0% (34/40) on control; risk difference -3.2 percentage points (95% CI -22.7 to 16.4), risk ratio 0.96 (0.76–1.22); unadjusted two-proportion z-test p = 0.744.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1: Phase II Mosunetuzumab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2: Phase II Rituximab + CHP-Pola (Randomized) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the efficacy picture beyond the primary PET-CT complete response assessment. They include complete response and overall response at the primary response assessment using CT-only criteria, overall response using PET-CT, best overall response, duration of response, progression-free survival, progression-free survival at 1 year, and event-free survival. The registry lists 17 outcome measures overall and posts 16 secondary outcomes. Secondary response measures were determined by investigators, whereas the primary endpoint was determined by an independent review committee.

Across the posted binary response outcomes, the estimates vary by endpoint and by study group. This is expected to some degree because the outcomes use different response definitions and imaging bases, and because the cohorts are not all part of the same randomized comparison. Group C, the mosunetuzumab plus CHOP cohort, is present in secondary results but was not part of the primary randomized contrast. The Phase II M-CHOP arm with no enrolled participants cannot contribute participant outcomes. Therefore, secondary results should be read according to their specific group, assessment, and role rather than as one pooled efficacy conclusion.

The secondary findings provide context for the primary result but do not replace it. A pattern across multiple outcome definitions can help show whether estimates are broadly similar or vary with measurement choice; it cannot establish a definitive treatment difference without considering uncertainty and the analysis plan. The registry does not report a multiplicity adjustment or a hierarchy for these outcomes. In general, testing or interpreting many endpoints without accounting for multiplicity makes isolated favorable or unfavorable results less persuasive, because chance variation can generate apparent differences among many comparisons.

Time-to-event outcomes such as duration of response, progression-free survival, and event-free survival address aspects of outcome over time rather than response status at a single assessment. Their interpretation depends on follow-up, event definitions, censoring, and analysis methods. These details are not reported in the information available for the posted endpoint summaries, so no time-to-event result should be inferred from their presence in the registry's outcome list.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• CR Rate at PRA Based on CT Only as Determined by the Investigator (Phase II)
• Overall Response Rate (ORR) at PRA Based on PET-CT as Determined by the Investigator (Phase II)
• ORR at PRA Based on CT Only as Determined by the Investigator (Phase II)
• Best ORR Based on PET-CT and/or CT Scan as Determined by the Investigator (Phase II)
• Duration of Response (DOR) as Determined by the Investigator (Phase II)
• Progression-free Survival (PFS) as Determined by the Investigator (Phase II)
• PFS at 1 Year as Determined by the Investigator (Phase II)
• Event-free Survival (EFS) as Determined by the Investigator (Phase II)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a proportion, since the registry reports the percentage of participants classified as having complete response. For each arm, the numerator is the number meeting the response definition and the denominator is the number included for that endpoint. The registry gives rates and confidence intervals, but does not give a detailed description of the endpoint denominator, handling of unevaluable participants, or missing response assessments in the primary record. Those details matter because different rules for incomplete assessments can affect a response proportion.

In general, a confidence interval describes uncertainty around an estimated quantity under the assumptions of the method used to construct it. The primary endpoint record reports 95% confidence intervals for each arm. A 95% confidence interval is not a guarantee that the true rate lies inside the particular interval; it is a procedure that, under its assumptions, would cover the true quantity in 95% of repeated samples. It is also not a range of individual participant outcomes. The method for the registry's arm-specific intervals is not stated in the record, so they cannot be fully assessed for their statistical assumptions from the posted information alone.

The registry's primary reported comparison is a difference in rates. The sign of a difference depends on which arm is subtracted from which; the registry reports -4.77, while the unadjusted recalculation is expressed for Arm 2 relative to Arm 1 as 0.048. These values are compatible with opposite direction conventions and different presentation scales, but the registry does not specify the calculation details needed to reconcile the intervals. The reported interval, -30.61 to 21.07, includes zero. The unadjusted recalculated interval, -0.175 to 0.271, also includes zero. General statistical interpretation: an interval including zero does not establish no effect; it indicates that the analysis does not rule out zero difference at the corresponding confidence level.

The recalculated comparison uses the posted summary statistics and is unadjusted. It is not adjusted for covariates, stratification, or other design features. The registry record does not report a method for the sponsor's primary analysis, and no p-value is listed for that reported analysis. The separate unadjusted recalculated p-value is 0.681. In general, a p-value measures how incompatible the data are with a specified null model under the test's assumptions; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. A p-value should be interpreted alongside the estimated difference and its confidence interval.

Randomization supports comparison by assigned group, but it does not remove sampling uncertainty. With 40.0 and 22.0 participants in the primary endpoint groups, the precision of estimated percentages and differences is limited. This is reflected by the broad reported confidence intervals. In general, small samples can produce unstable estimates, especially for outcomes expressed as proportions, because each participant represents a relatively substantial part of the group.

The trial included multiple phases, arms, and outcome measures. The registry lists 17 outcome measures, and 16 secondary outcomes are posted. It lists one reported analysis for the primary result. In general, when many outcomes or comparisons are examined, the chance of seeing apparently notable results by chance can increase. A prespecified hierarchy or multiplicity adjustment can help control that risk, but such details are not reported for the analyses summarized in the registry record. This limits how strongly secondary comparisons can be interpreted.

For proportions, the normal approximation used in the separate planning illustration is a general statistical method that treats the estimated difference as approximately normally distributed. Its accuracy depends on conditions such as the group sizes and outcome proportions. General concept: when the outcome is binary, the variance of a proportion depends on the probability of the event; it is not constant across all possible response rates. Exact or alternative interval methods can behave differently, particularly with small groups, but the registry's method for its own reported interval is not identified. No additional method should be assumed from the summary values alone.

The registry defines the primary efficacy population as the intent-to-treat population, consisting of all participants. It also says the primary efficacy analysis compared Arm 1 with Arm 2 according to treatment assigned at randomization, and that analyses for Arms A1, A2, and B were exploratory. The record does not describe how missing observations were handled, whether any participants were excluded from the endpoint analysis, or how protocol deviations were addressed. Those details are important for understanding whether the stated population and the analyzed denominators align exactly.

11. Confidence Intervals and Precision

The primary arm-specific estimates are 72.5% for Arm 1, with a 95% confidence interval of 56.11 to 85.4, and 77.3% for Arm 2, with a 95% confidence interval of 54.63 to 92.18. These intervals cover broad ranges of possible response rates. In particular, each arm's interval includes values appreciably below and above its point estimate, so the exact underlying proportion is not pinned down closely by these data.

The registry-reported difference in rates is -4.77, with a 95% confidence interval from -30.61 to 21.07. This wide interval crosses zero and accommodates differences in either direction. The recalculated unadjusted risk difference for Arm 2 relative to Arm 1 is 0.048, with a 95% confidence interval from -0.175 to 0.271. The intervals are reported on different presentation scales and with different direction conventions. Each includes the no-difference value, and each allows a range of potentially meaningful differences; the posted sample is not precise enough to resolve the contrast narrowly.

In general, interval width reflects both the amount of information in the data and the method used to calculate uncertainty. Smaller groups tend to yield less precise estimates, though precision also depends on the observed rate and statistical method. The primary comparison includes 40.0 and 22.0 participants, and the corresponding uncertainty is substantial. A confidence interval does not convey whether a difference matters clinically; that requires a context and a threshold, neither of which is reported for the primary comparison.

The reported interval's construction method is not reported in the registry record. Consequently, the displayed estimates support a descriptive reading of uncertainty, but a full audit of the statistical procedure is not possible from the registry information alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial's original design calculation. For these binary outcomes, the figures are participants per arm; time-to-event planning figures, when present, are total numbers of events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry's original sample-size justification and assumptions are not reported in the registry record.

The 80% power column means the planned design would have an 80% chance of detecting an effect of the chosen size under the stated assumptions, if that effect were the true one and the statistical model were appropriate. The 90% power column uses a higher target probability of detecting that same specified effect. These values are planning quantities rather than descriptions of what happened in the completed trial. They are not observed power.

Planning for 100% of the observed effect uses the full observed estimate as the target effect. Planning for 75% of the observed effect and 50% of the observed effect asks what would be needed to detect smaller effects. The smaller the effect to be detected, the more participants are generally needed to distinguish it from random variation while maintaining the same power target and other assumptions. These illustrations are especially sensitive when the observed estimate comes from small groups, because that estimate itself can be imprecise.

The values should not be read as recommendations for this study or as evidence that the original trial was adequately or inadequately sized. They are hypothetical planning comparisons using the listed assumptions, not a substitute for the unreported protocol rationale, a prespecified clinically important difference, or the original analysis plan.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.725; treatment proportion p₁ = 0.773; average p̄ = 0.749.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6133 = 1.2020.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6124 = 0.5154.
4. n = (1.2020 + 0.5154)² / (0.0477)² = 1,294.9, rounded up to 1,295 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.725                          # control proportion
p1 <- 0.772727272727273                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3677141)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,295 (80% power), 1,733 (90% power)
 75% of observed effect: n per arm = 2,339 (80% power), 3,131 (90% power)
 50% of observed effect: n per arm = 5,343 (80% power), 7,152 (90% power)
power.prop.test: 1294.9 
Simulated power at n = 1,295 per arm: 0.799 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the primary comparison as a difference in rates of -4.77, with a 95% confidence interval from -30.61 to 21.07. It does not list a p-value or identify the method used for that reported analysis. The primary endpoint information specifies that the comparison was between the randomized arms and that participants were grouped according to their assigned treatment.

The unadjusted recalculation from the posted arm summaries expresses the contrast as Arm 2 relative to Arm 1: risk difference 0.048, with a 95% confidence interval from -0.175 to 0.271 and an unadjusted p-value of 0.681. The difference in signs is consistent with describing the contrast in opposite directions; the values also appear in different scales. The registry does not report enough methodological detail to establish why the interval limits differ, so they should not be treated as identical calculations expressed only in another format.

The recalculation is a simple comparison from posted summary statistics. It does not reproduce any adjustment or other procedure that may have been used in the registry's analysis, since those details are not reported. The registry does not flag a discrepancy. The sponsor's reported estimate remains the trial's posted analysis, while the recalculation offers a transparent, unadjusted perspective on the same summary data. Neither estimate is precise enough to rule out a range of differences in either direction.

15. Multiplicity, Missing Data and Analysis Populations

The study has multiple phases, treatment groups, and efficacy outcomes. The registry lists 17 outcome measures and posts 16 secondary outcomes, while one analysis is listed for the primary result. With many endpoints or comparisons, chance alone can produce apparently noteworthy estimates. In general, multiplicity procedures or a prespecified testing hierarchy can help control the overall risk of false-positive findings. Whether such procedures were used, and how secondary outcomes were prioritized, is not reported in the registry record.

The primary efficacy population is described as the intent-to-treat population consisting of all participants, and the primary analysis compared Arm 1 with Arm 2 according to randomized assignment. Efficacy analyses for Arms A1, A2, and B are described as exploratory. These statements clarify the intended population and the role of some analyses, but they do not explain how participants with missing endpoint assessments were handled. Missing-data rules, imputation methods, and sensitivity analyses are not reported in the registry record.

Missing outcome data can affect a binary response rate if the probability of missing assessment differs across participants or groups. In general, treating missing outcomes as non-response, excluding them, or using a model-based method can lead to different estimates. The endpoint record gives arm sample sizes and response percentages, but the registry information does not specify whether those sample sizes are the full intent-to-treat denominators for this outcome or whether any response assessments were unavailable.

The record also does not report details of protocol deviations, analysis-set exclusions, or sensitivity analyses addressing alternative assumptions. Nor does it provide the complete statistical analysis plan, so it is not possible to determine whether the registered primary analysis was carried out exactly as planned or whether analysis choices were made after results were known. These absences do not establish that the analyses were inappropriate; they limit how independently the analysis can be evaluated from the registry record.

Finally, the open-label design is relevant to outcomes that depend on decisions or assessments potentially influenced by knowledge of treatment. Independent committee assessment for the primary PET-CT endpoint may reduce some risks associated with unmasked treatment, but the registry does not describe the committee's procedures. Investigator-determined secondary endpoints remain a distinct assessment source, and should be interpreted with that distinction in mind.

16. 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: febrile neutropenia (50.0%), supraventricular tachycardia (33.3%), pneumocystis jirovecii pneumonia (33.3%), sepsis (33.3%), malignant neoplasm progression (33.3%).

The serious adverse event figures are presented by registry group, with numbers at risk and numbers affected. For the randomized groups, 38 participants were at risk in Arm 1 and 24 were reported as affected; in Arm 2, 22 were at risk and 3 were affected. These counts describe the registry's group-level serious adverse event reporting. They are not a randomized comparison adjusted for differences in follow-up, exposure, or participant characteristics.

The registry also reports other adverse events: 38 of 38 at risk in Arm 1 and 22 of 22 at risk in Arm 2 were affected. Deaths are listed as 5 in Arm 1 and 3 in Arm 2. The record does not establish from these counts whether deaths were caused by treatment or disease, nor does the count alone describe timing or clinical context. Serious adverse event terms listed among the most frequent include febrile neutropenia, supraventricular tachycardia, Pneumocystis jirovecii pneumonia, sepsis, malignant neoplasm progression, and hypotension. Their listed percentages are 50.0% and 33.3% for the specified terms; the denominator for these percentages is not explained in the available record.

Safety counts across the entire study include different phases and treatment groups, so they should not be combined or compared without regard to group definitions. The registry's counts describe reported events, not individual risk predictions or treatment causality.

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

The primary endpoint shows complete response proportions of 72.5% in the mosunetuzumab plus CHP-polatuzumab vedotin randomized arm and 77.3% in the rituximab plus CHP-polatuzumab vedotin arm at the scheduled primary response assessment. The confidence intervals are broad, and the registry-reported difference interval crosses zero. The results therefore describe observed response rates but do not precisely establish the size or direction of a difference between the randomized regimens.

The results do not demonstrate that the regimens are equivalent. A conclusion of equivalence requires a prespecified margin and a design and analysis tailored to that question; such a margin is not reported. The data also do not establish that one regimen is superior based on the reported primary endpoint: the registry's interval includes no difference, and the analysis does not report a p-value. A numerical contrast should not be read as proof of a treatment effect.

The primary endpoint is a response assessment at one defined time point. It does not by itself describe durability of response, survival, symptoms, quality of life, or longer-term outcomes. The registry lists other endpoints addressing some different dimensions, but their presence does not turn the primary response result into a broader conclusion. Each endpoint has its own definition, assessment method, and uncertainty.

These findings also apply to the population and comparison represented by the randomized Phase II groups, not automatically to every participant in the broader Phase Ib/II study. The registry includes dose-finding cohorts and a separate CHOP cohort, and the primary efficacy analysis is specifically the randomized Arm 1 versus Arm 2 comparison. The study record does not provide enough information about missing data or analysis details to independently assess all aspects of the endpoint calculation.

In general, clinical interpretation requires weighing the estimate, its uncertainty, the endpoint's relevance, and the study design together. The posted data support a cautious description of the observed proportions and a wide range of plausible differences. They do not support medical advice or a definitive claim about comparative benefit.

18. Why This Trial Matters Statistically

This trial is statistically notable for combining dose-finding and randomized Phase II evaluation within one study record. That structure creates several distinct populations and questions: dose selection, safety and tolerability, pharmacokinetics, and comparative efficacy. Keeping those components separate is essential. The primary efficacy question is not answered by pooling every listed treatment group or by treating total enrollment as the randomized comparison sample.

The primary contrast is randomized, which is an important design feature for estimating differences between assigned groups. At the same time, the endpoint groups include 40.0 and 22.0 participants, and the resulting confidence intervals are broad. Randomization reduces some sources of systematic imbalance in expectation, but it cannot eliminate uncertainty from limited group sizes. The endpoint estimates therefore illustrate the distinction between a point estimate and the precision with which it is known.

The study also shows why a response proportion should not be interpreted in isolation. The primary endpoint uses PET-CT and independent review, while secondary response outcomes include investigator-determined assessments and CT-only measures. Different definitions can yield different estimates, and multiple outcomes bring multiplicity concerns. The distinction between a primary endpoint and exploratory or secondary results is statistically important, not merely a labeling choice.

Finally, the registry record makes some design features clear while leaving other analytic details unavailable. It identifies randomization, open-label status, the intent-to-treat population, and the primary comparison, but it does not report the original sample-size rationale, method for the sponsor's interval, multiplicity plan, or handling of missing data. Recognizing what is and is not documented helps readers separate observed evidence from assumptions that cannot be checked.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary randomized comparison is based on 40.0 participants in Arm 1 and 22.0 in Arm 2. The response estimates consequently have broad confidence intervals, and the difference estimate is imprecise. The unequal endpoint group sizes also mean that the two arm estimates do not have identical precision. These limitations constrain the strength of conclusions from the primary response comparison.

The study is Phase Ib/II and includes dose-finding cohorts, a safety cohort, and randomized Phase II groups. Its overall enrollment of 117 should not be mistaken for the primary comparison's analysis size. The broader study population and treatment groups are not all interchangeable, and some efficacy analyses are described as exploratory. The Phase II M-CHOP 1L DLBCL arm had no participants enrolled, according to the registry.

The study was open-label. The primary outcome was assessed by an independent review committee, but the registry does not report the committee's procedures. Several secondary outcomes were determined by investigators, making their assessment source distinct from the primary endpoint. The registry also does not report the original sample-size rationale, detailed analysis method for the primary result, missing-data approach, or multiplicity plan. These omissions limit independent evaluation of the analysis.

The primary response measure is a point-in-time endpoint assessed 6-8 weeks after either C6D1 or the last dose of study treatment. It does not provide a direct measure of response duration or longer-term outcomes. Those outcomes are listed separately, but the information summarized for the primary comparison does not establish their results. The confidence intervals and reported analysis should be interpreted only for the endpoint and comparison to which they apply.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase Ib/II Study Investigating the Safety, Tolerability, Pharmacokinetics, and Efficacy of Mosunetuzumab (BTCT4465A) in Combination With CHOP or CHP-Polatuzumab Vedotin in Participants With B-Cell Non-Hodgkin Lymphoma — NCT03677141.
• Registry record last updated 2024-12-18; status last verified 2024-11.
• Results first posted 2024-12-18.
• 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.

23. Record Summary

NCT03677141 is a completed, open-label, randomized, controlled, multicenter Phase Ib/II study of mosunetuzumab combinations in B-cell non-Hodgkin lymphoma. The primary randomized Phase II comparison evaluated mosunetuzumab plus CHP-polatuzumab vedotin against rituximab plus CHP-polatuzumab vedotin. The primary endpoint was complete response at the primary response assessment based on PET-CT, determined by an independent review committee.

The registry reports response rates of 72.5% and 77.3%, respectively, with broad 95% confidence intervals. Its reported difference in rates was -4.77, with a 95% confidence interval from -30.61 to 21.07. An unadjusted recalculation gives a risk difference of 0.048 for Arm 2 relative to Arm 1, with a 95% confidence interval from -0.175 to 0.271. Both convey substantial uncertainty and include no difference under their respective presentations. Details of the sponsor's calculation method, missing-data handling, multiplicity procedures, and original sample-size rationale are not reported in the registry record.