To Compare Efficacy and Safety Between CT-P10 and Rituxan in Patients With Low Tumour Burden Follicular Lymphoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Compare Efficacy and Safety Between CT-P10 and Rituxan in Patients With Low Tumour Burden Follicular Lymphoma (NCT02260804), a randomized phase 3 study. The primary outcome is Primary Efficacy Endpoint - Overall Response Rate by 7 Months.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group, active-controlled study sponsored by Celltrion. The registry lists quadruple masking; the official study title describes the study as double-blind. The registry record does not explain the relationship between those masking descriptions. The recorded enrollment was 258, and the study status is completed.

The comparison used two active treatment strategies. Both groups received the same stated dose intravenously over 4 induction cycles. The maintenance descriptions differ: the CT-P10 group continued CT-P10, while the Rituxan group received Rituxan for its first 6 maintenance cycles and CT-P10 for its last 6. This means the study comparison concerns the assigned treatment strategies as described, including their maintenance regimens, rather than a comparison in which every maintenance cycle differed only by the product name.

The primary endpoint was assessed by 7 months, during Month 7, up to Maintenance Cycle 3 or Week 28. The record lists overall response rate over the study period as a secondary efficacy outcome, with a timeframe of up to 27 months. Other listed secondary outcomes concern B-cell kinetics, pharmacokinetic measures, progression-free survival, overall survival and time to progression.

The study began on 2015-11-09, and its primary completion date was 2018-01-04. The registry record does not report the trial's original sample-size justification or the details of its planned statistical analysis. Those absences matter when interpreting the sponsor's equivalence analysis and the separate unadjusted recalculation: the posted evidence does not establish that every aspect of the analysis can be reconstructed from the registry entry.

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.

Before assignment: A total of 402 participants were screened for the study. Of those, 144 participants failed screening and 258 participants were enrolled in the study.

Induction Study Period

Reasons for not completing this period:

1st Year of the Maintenance Period (MP1)

Reasons for not completing this period:

2nd Year of the Maintenance Period (MP2)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population consisted of all patients enrolled and randomly assigned to receive a study drug, regardless of whether or not any study drug dosing was completed.

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 Primary Efficacy Endpoint - Overall Response Rate by 7 Months, measured over During the Month 7 (up to Maintenance Cycle 3; Week 28).

The primary endpoint was overall response rate by 7 months. It measures the proportion of participants whose best response by the specified assessment time was complete response, unconfirmed complete response or partial response, as determined by central review. The registry describes response assessment using the 1999 IWG criteria and contrasted CT and/or MRI. It gives definitions based on disappearance or regression of disease findings, including changes in target lesions and whether new lesions or progression were present.

A response-rate endpoint is binary at the participant level: each person is classified according to whether the defined response occurred by the assessment time. In general, binary endpoints can be summarized by the number of participants meeting the definition and the number evaluated, as well as by a difference between groups. This makes the clinical contrast relatively direct to describe, but it does not show the duration of a response or capture every aspect of disease course.

The time limit is part of the endpoint definition. A response recorded by 7 months answers a different question from response at any point over the study period, which is why the later overall response outcome is listed separately. The registry's primary population was intention-to-treat: all enrolled and randomized patients, regardless of whether they completed study-drug dosing. The record does not report how missing or unevaluable response assessments were handled.

7. Results Posted in the Registry

• Rituxan: 81.2% (104/128) versus 83.1% (108/130) on control; risk difference -1.8 percentage points (95% CI -11.2 to 7.5), risk ratio 0.98 (0.87–1.10); unadjusted two-proportion z-test p = 0.701.

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.

Secondary Efficacy Endpoint - ORR Over the Study Period

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Rituxan: 87.5% (112/128) versus 83.8% (109/130) on control; risk difference 3.7 percentage points (95% CI -4.9 to 12.2), risk ratio 1.04 (0.94–1.15); unadjusted two-proportion z-test p = 0.402.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituxan and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning overall response over the study period, B-cell kinetics, pharmacokinetic measures, progression-free survival, overall survival and time to progression. Numerical results are posted for the longer-period overall response outcome. Numerical results for the remaining listed secondary outcomes are not reported in the registry record.

The longer-period response outcome addresses a different observation window from the primary response assessment by 7 months. It can add context about responses recorded over the study period, but it does not replace the primary endpoint or establish the results of the unreported survival and time-to-event outcomes. The overall pattern across the listed secondary outcomes therefore cannot be fully assessed from the posted results.

In general, secondary outcomes are often interpreted with more caution when many outcomes are examined. The more comparisons considered, the greater the chance that some results will appear notable by chance alone. An unadjusted result does not account for that multiplicity, and the registry record does not report a multiplicity adjustment or a hierarchy for secondary testing. Secondary findings can inform the broader picture, but they carry less confirmatory weight than a prespecified primary result when their testing context is unclear. No conclusion about unreported secondary measures should be inferred from the primary response result.

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

• Secondary Efficacy Endpoint - ORR Over the Study Period
• Secondary PD Endpoint - B-cell Kinetics (B-cell Depletion and Recovery)
• Secondary PK Endpoints - Cmax
• Secondary PK Endpoints - Ctrough
• Secondary Efficacy Endpoint - Progression-free Survival (PFS)
• Secondary Efficacy Endpoint - Overall Survival (OS)
• Secondary Efficacy Endpoint - Time-to Progression (TTP)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either met the response definition by 7 months or did not. The registry posts counts for each group and an unadjusted recalculation comparing the response proportions. In general, a proportion describes the share of a group with the outcome, while a risk difference expresses the absolute contrast between two such proportions. A risk difference of zero corresponds to equal proportions; values on either side represent different directions of contrast, depending on which group is subtracted from which.

What does the confidence interval add?

In general, a confidence interval describes the uncertainty around an estimated contrast under the statistical method used. It indicates a range of values compatible with the data and method; it is not a guarantee that the true value lies within that range. For this primary recalculation, the interval crosses zero. That means the posted data do not distinguish a difference in one direction from a difference in the other direction at the level implied by that interval. The interval's breadth also matters: it allows a range of possible contrasts rather than pinning the result to a single precise value.

How is an equivalence analysis different?

In general, an equivalence analysis asks whether the difference is sufficiently small to lie inside prespecified acceptable limits. It is not established merely because a conventional test fails to reject a no-difference hypothesis. An equivalence margin must define the limits, and the analysis must be interpreted against those limits. The registry reports a sponsor analysis labelled equivalence, with a 90% confidence interval, but the margin and analytical details are not reported in the registry record. The sponsor's stated analysis should therefore be distinguished from the unadjusted recalculation, which is a simple comparison of the posted summary counts.

What does unadjusted mean?

In general, an unadjusted comparison uses the observed group summaries without controlling for other variables. It can be useful as a transparent description of the posted results, but it may not match an analysis that accounts for stratification, covariates, missing outcomes or other design features. The registry record does not report enough detail to determine whether or how such features entered the sponsor's analysis. The recalculation should therefore be read as a straightforward summary-based comparison, not as a reconstruction of the sponsor's full model.

Why does the analysis population matter?

The registry defines the primary intention-to-treat population as all enrolled and randomized patients, regardless of whether study-drug dosing was completed. In general, an intention-to-treat analysis preserves the randomized group assignment and is intended to estimate outcomes for participants as assigned. Its interpretation still depends on how missing endpoint values are handled. That handling is not reported in the registry record, so the posted population definition alone does not resolve whether every randomized participant had an assessable primary outcome or how any unavailable assessment was treated.

Why can over-dispersion matter?

In general, over-dispersion arises when observed variability exceeds what a statistical model assumes. It can make standard errors too small if the model fails to allow for the extra variability, leading to confidence intervals that are too narrow. The primary endpoint is a participant-level binary response, and no over-dispersion adjustment is described in the registry record. This general issue should not be taken to imply that over-dispersion was present or that a particular model was used; the analysis method is not reported in enough detail to make that assessment.

The primary response criteria also shape the statistical result. Central review and the specified response categories provide a defined basis for classifying outcomes, while the assessment deadline fixes the period in which a response counts. These choices improve clarity about what was measured, but they do not remove uncertainty from the estimated group comparison. The separate overall response outcome over the study period addresses a longer observation window and should not be treated as the same endpoint.

11. Confidence Intervals and Precision

The primary unadjusted recalculation has a confidence interval that extends across zero, so the posted summary data are compatible with a contrast in either direction. This is a statement about uncertainty in the estimated difference, not a conclusion that the groups are identical. The interval's limits are displayed with the primary results; they should be considered alongside the estimate and the response counts rather than interpreted as a range of likely participant outcomes.

The sponsor's reported equivalence analysis has a 90% confidence interval from -6.43 to 10.2 around a reported difference in proportion of 1.8. Its precision cannot be judged against an equivalence standard without the margin defining acceptable differences. That margin is not reported in the registry record. The interval alone therefore does not show whether the sponsor's criterion for equivalence was met.

In general, a confidence interval depends on the observed data and the statistical method. Wider intervals indicate greater uncertainty about the contrast; narrower intervals indicate greater precision under the same method. Precision is not the same as clinical importance: a narrow interval can still cover differences that matter, while a broad interval can leave important possibilities unresolved. Here, the primary result should be read as an estimate with uncertainty, not as a precise demonstration of sameness. The registry record does not report the full analysis details needed to assess whether the sponsor's interval and the unadjusted interval target exactly the same contrast.

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 for participants per arm because the outcomes used in this calculation are binary participant outcomes, not time-to-event totals. In general, a sample-size curve relates the assumed effect to the number of participants needed under stated design assumptions. Read its values as planning illustrations for a future study, not as a description of enrollment in this completed trial.

The calculation assumes 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 a stated fraction of the observed effect. The columns for 80% and 90% power describe the number of participants per arm under those assumptions to have the corresponding probability of detecting the assumed effect, if that effect and the calculation assumptions hold. They do not indicate the probability that the trial's conclusion is correct.

Planning for 75% of the observed effect requires more participants per arm than planning for the full observed effect; planning for 50% requires still more. This is the general pattern because smaller differences are harder to distinguish from random variation. The exact figures are illustrations based on the observed effect, not the original trial's design assumptions, which are not reported in the registry record. These values are not observed power.

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 = 0.831; treatment proportion p₁ = 0.812; average p̄ = 0.822.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5414 = 1.0611.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5412 = 0.4555.
4. n = (1.0611 + 0.4555)² / (-0.0183)² = 6,891.5, rounded up to 6,892 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 <- 0.830769230769231                          # control proportion
p1 <- 0.8125                          # 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(2260804)
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 = 6,892 (80% power), 9,226 (90% power)
 75% of observed effect: n per arm = 12,130 (80% power), 16,238 (90% power)
 50% of observed effect: n per arm = 27,013 (80% power), 36,162 (90% power)
power.prop.test: 6891.5 
Simulated power at n = 6,892 per arm: 0.803 (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 a sponsor analysis categorized as equivalence, with a difference in proportion of 1.8 and a 90% confidence interval from -6.43 to 10.2. The registry record does not report the equivalence margin, the detailed analysis method, or the direction convention for the difference. Those details are important for interpreting the sponsor's result and for comparing it directly with another estimate.

The separate recalculation uses the posted group counts to make an unadjusted comparison. It reports a risk difference, an interval that crosses zero and an unadjusted p-value of 0.701. This simple recalculation is not a substitute for the sponsor's own analysis: the analyses may differ in estimand, coding, model or handling of study features, and the registry entry does not provide enough detail to reconcile them fully. The sponsor's analysis takes precedence when describing the sponsor's reported equivalence assessment. Its label should not be treated as independently verified without the margin and analysis details needed to assess the equivalence criterion.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is overall response rate by 7 months, while the registry lists multiple secondary efficacy, pharmacodynamic and pharmacokinetic outcomes. Considering multiple outcomes raises a multiplicity question: in general, repeated testing can increase the chance of at least one apparently notable result even when there is no real effect on the outcomes being tested. Statistical plans may address this through a prespecified hierarchy or adjustment, but the registry record does not report whether either approach was used for secondary outcomes.

The record lists one sponsor analysis for the primary endpoint and does not provide a detailed statistical analysis plan. The equivalence margin, the full analysis method and the approach to secondary testing are not reported in the registry record. Without those details, the sponsor's equivalence result can be described as reported, but its testing framework cannot be reconstructed from this entry alone. The unadjusted recalculation should not be mistaken for the planned sponsor analysis or for a multiplicity-adjusted result.

The primary population is defined as all enrolled and randomized patients, whether or not they completed dosing. This clarifies the intended population for the primary endpoint, but it does not state how missing response assessments were handled. The record does not report the number of missing or unevaluable primary assessments, imputation methods, sensitivity analyses or whether any alternative analysis populations were used. Missing outcome data can affect a response-rate estimate if assessment availability differs between groups or if the handling assumptions are not appropriate; the available record does not allow those possibilities to be evaluated.

Randomization and masking are design features that can support a fair comparison, but neither resolves multiplicity or missing-data questions. The registry lists randomized allocation and quadruple masking, while the official title uses the term double-blind. Details of implementation and of the analysis plan are not reported. These limitations constrain how far the posted primary and secondary results can be interpreted beyond their stated endpoints and populations.

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: pneumonia (1.6%), angina unstable (0.8%), atrial fibrillation (0.8%), hyperparathyroidism (0.8%), intestinal polyp (0.8%).

The registry records serious adverse events for 14 participants in the CT-P10 group and 14 in the Rituxan group. It records other adverse events for 93 participants in the CT-P10 group and 86 in the Rituxan group. The listed deaths are 3 in each group. These are descriptive counts; they do not by themselves establish whether an event was caused by study treatment or whether the groups differ meaningfully in safety.

The registry also lists pneumonia at 1.6% and angina unstable, atrial fibrillation, hyperparathyroidism, intestinal polyp and pancreatitis at 0.8% each among the top serious adverse-event terms. The record does not give further detail for these terms in the adverse-event summary. In general, adverse-event counts need to be considered in relation to the number at risk, duration of observation, event definitions and clinical context. The posted figures should not be treated as a complete characterization of safety or as evidence that one regimen is safer.

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

The primary result describes the proportion of randomized participants who met a central-review response definition by 7 months. The posted counts show responses in both groups. The unadjusted recalculation has an interval spanning zero, so it does not provide clear evidence of a difference in either direction. At the same time, uncertainty across a range of possible contrasts means that absence of a clear difference is not proof that the treatment strategies are equivalent.

The sponsor's reported equivalence analysis is relevant to the stated study objective, but the registry record does not give its equivalence margin or full analysis details. Equivalence is a conclusion tied to prespecified limits, not simply the absence of a statistically significant difference. The sponsor's report can be presented as an equivalence analysis, while the available registry entry is insufficient to independently assess the decision against its margin.

The result applies to the described randomized treatment strategies and this study population. In particular, the maintenance regimens were not identical: the CT-P10 group continued CT-P10, whereas the Rituxan group switched to CT-P10 for its last 6 maintenance cycles. The primary response endpoint also has a defined time horizon and does not answer questions about response duration, progression-free survival, overall survival or time to progression.

The registry's secondary outcome list provides a broader set of questions, but numerical results for most listed outcomes are not reported in the registry record. Adverse-event counts are descriptive and do not establish causation. Accordingly, the posted results support a narrow statistical interpretation of the observed response counts and the reported sponsor analysis; they do not establish a general claim about long-term outcomes, all aspects of safety or the performance of either product in settings beyond the trial described.

18. Why This Trial Matters Statistically

This trial illustrates why an equivalence question requires more than observing similar-looking response counts or a non-significant test of difference. The statistical claim depends on a prespecified margin that defines how much difference would still count as acceptably small. The sponsor's analysis is labelled equivalence, but the margin is not reported in the registry record. That missing detail limits independent interpretation of the claim.

It also demonstrates the distinction between a sponsor analysis and a simple recalculation from posted summary statistics. The latter makes the contrast and its uncertainty accessible, but it may not reproduce the sponsor's estimand or methods. Transparent reporting of the analysis population, endpoint handling, model, missing-data approach and equivalence boundaries is important for evaluating whether different analyses answer the same question.

The design's regimen details matter statistically as well as clinically. Both groups had the same stated induction drug and dose, while the maintenance descriptions differ in the sequence of products. The randomized comparison therefore concerns those assigned strategies as recorded. It should not be reduced to an uncomplicated comparison of two products across every treatment cycle.

Finally, the trial highlights the importance of distinguishing a fixed-time response endpoint from longer-term outcomes and of interpreting secondary results in light of multiplicity. The registry lists several further outcomes, but their numerical results are not reported in the registry record. A careful account separates what the primary response data show from what remains unresolved about equivalence criteria, longer-term efficacy and safety.

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.

Several limitations specific to this registry record constrain interpretation. The sponsor's primary analysis is labelled equivalence, but its margin and detailed statistical method are not reported. Without those details, the sponsor's conclusion cannot be independently evaluated against the intended equivalence criterion using the registry entry alone. The unadjusted recalculation is informative as a summary-based comparison but should not be treated as a replacement for the sponsor analysis.

The treatment schedules also differ during maintenance. The Rituxan group received CT-P10 for its last 6 maintenance cycles, while the CT-P10 group received CT-P10 throughout its described induction and maintenance schedule. This means that the contrast is between the regimens as assigned, and the record does not permit attribution of every outcome to a product comparison isolated from treatment sequence.

The primary endpoint is response by 7 months, whereas the listed secondary overall response outcome extends up to 27 months. The primary endpoint does not directly measure response duration, progression or survival. Although progression-free survival, overall survival and time to progression are listed, their numerical results are not reported in the registry record. That limits assessment of how the response finding relates to longer-term outcomes.

The registry defines the intention-to-treat population but does not report missing-assessment handling, endpoint imputation, sensitivity analyses or detailed baseline characteristics. It also does not report the multiplicity approach for secondary outcomes. These gaps do not invalidate the posted counts, but they limit the assessment of bias, precision and confirmatory status. The record's description of quadruple masking and the official title's double-blind wording are not reconciled in the entry.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: To Compare Efficacy and Safety Between CT-P10 and Rituxan in Patients With Low Tumour Burden Follicular Lymphoma — NCT02260804.
• Registry record last updated 2021-04-08; status last verified 2021-02.
• Results first posted 2021-04-08.
• 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

NCT02260804 is a completed phase 3 randomized, parallel-group, active-controlled study sponsored by Celltrion in patients with low tumour burden follicular lymphoma. The registry records enrollment of 258 and lists quadruple masking. The primary endpoint was overall response rate by 7 months, assessed by central review in the intention-to-treat population.

The posted primary counts are 108 of 130 in the CT-P10 group and 104 of 128 in the Rituxan group. The sponsor's analysis is labelled equivalence and reports a difference in proportion of 1.8 with a 90% confidence interval from -6.43 to 10.2. The registry record does not report the equivalence margin or full analysis details. The unadjusted recalculation has a confidence interval spanning zero and an unadjusted p-value of 0.701.

Results for most listed secondary outcomes are not reported in the registry record. Adverse-event counts are descriptive and do not establish causation or comparative safety.