Bortezomib After Combination Chemotherapy, Rituximab, and an Autologous Stem Cell Transplant in Treating Patients With Mantle Cell Lymphoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bortezomib After Combination Chemotherapy, Rituximab, and an Autologous Stem Cell Transplant in Treating Patients With Mantle Cell Lymphoma (NCT00310037), a randomized phase 2 study. The primary outcome is Progression-free Survival Rate at 18 Months.

2. Clinical Question

This is a comparison of two schedules and treatment strategies, not a comparison of bortezomib with no bortezomib. Both arms received bortezomib after the intensive treatment described in the registry record. The outcome therefore addresses the posted contrast between maintenance and consolidation in this treatment context; it cannot isolate the effect of bortezomib versus receiving no bortezomib.

3. Trial Design

The registry record describes a randomized, open-label, parallel-group phase II trial. The study is listed as completed, with enrollment of 151. Its title and summary place the bortezomib strategies after combination chemotherapy, rituximab, and autologous stem cell transplantation for previously untreated mantle cell lymphoma. The registry record lists the start as 2006-06 and primary completion as 2013-12.

Arm A used a maintenance schedule: bortezomib 1.6 mg/m^2 intravenously on days 1, 8, 15, and 22, then a 4 week rest period. A cycle was 8 weeks, and up to 10 cycles were planned unless disease progression or unacceptable toxicity occurred. Arm B used a consolidation schedule: bortezomib 1.3 mg/m^2 intravenously on days 1, 4, 8, and 11 in a 3 week cycle, with up to 4 cycles unless progression or unacceptable toxicity occurred. Thus the comparison changes both the schedule and the duration of the planned course; it is not simply a comparison of two labels for the same regimen.

Masking is listed as none. The registry record does not report the allocation ratio, the process used to generate or conceal the randomization sequence, or whether any stratification factors were used. It also does not report the original sample-size justification or detailed eligibility criteria in the posted results summarized by the registry. Those omissions limit what can be said about the design beyond its randomized, parallel, phase II structure. The primary completion date does not itself describe when individual participants were assessed or how long follow-up continued.

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: Of the 147 participants who began treatment, 102 participants were randomized. Participants who were not randomized are excluded from all analyses per study design.

Overall Study

Reasons for not completing this period:

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.

Population: 102 participants were randomized. Participants who were not randomized are excluded from all analyses per study design.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival Rate at 18 Months, measured over At 18 months.

The primary endpoint is the progression-free survival rate at 18 months, expressed as a percentage of participants. The registry defines it as the proportion of patients who were both alive and progression-free 18 months after registration. It says the estimate was calculated using the Kaplan-Meier method.

Progression-free survival combines two clinically relevant events: disease progression and death. A participant who experiences either event before the assessment time is not counted as alive and progression-free at that time. This makes the endpoint a time-to-event measure, even though the result is presented as a rate at a specified time point. Kaplan-Meier estimation is generally used for time-to-event outcomes because participants may have different lengths of observed follow-up; participants without a recorded event can contribute information up to their last known follow-up. The registry record does not report the censoring rules or the details of follow-up used for this analysis.

A fixed-time estimate can communicate the proportion expected to remain alive and progression-free at a particular point in follow-up. It does not show the full pattern of events over time, and it does not by itself establish why outcomes differed or whether the contrast is precise enough to support a clear distinction between strategies. The accompanying confidence intervals and arm contrast are therefore important for interpreting the estimate.

7. Results Posted in the Registry

• Arm B Consolidation Therapy: 96.0% (48/50) versus 88.5% (46/52) on control; risk difference 7.5 percentage points (95% CI -2.7 to 17.8), risk ratio 1.09 (0.97–1.22); unadjusted two-proportion z-test p = 0.157.

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.

Number of Participants With Complete Response Intensive Chemo-immunotherapy Plus Maintenance or Consolidation Bortezomib

• 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:
  • Arm B Consolidation Therapy: 43.8% (35/80) versus 59.6% (31/52) on control; risk difference -15.9 percentage points (95% CI -33.1 to 1.3), risk ratio 0.73 (0.53–1.03); unadjusted two-proportion z-test p = 0.075.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B Consolidation Therapy and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists overall survival, complete response, and adverse-event outcomes as secondary outcomes. The posted quantitative information is incomplete across those outcomes: the complete-response figures and adverse-event summaries are available, while a quantitative overall-survival result is not reported in the registry record. The complete-response analysis uses different arm denominators from the primary endpoint, and the reason is not reported. The results should therefore be interpreted outcome by outcome rather than combined into a single overall judgment.

These secondary outcomes can provide additional context about response and safety, but they do not replace the primary progression-free survival comparison. Nor do they independently confirm the primary finding: they measure different outcomes and are subject to their own follow-up, measurement, and analysis limitations. The registry record does not report a complete set of sponsor analyses for the secondary outcomes, so a full assessment of their uncertainty and consistency is not possible.

Unadjusted secondary results generally carry less weight because a study may examine multiple outcomes, creating more opportunities for apparently notable results to arise by chance. A multiplicity plan can account for that issue by specifying how interpretation or statistical thresholds change across outcomes. Such a plan is not reported in the registry record. This does not establish that no multiplicity considerations were used; it means they cannot be evaluated from the posted information. The secondary findings are best treated as descriptive or exploratory evidence unless the registry record documents a prespecified inferential framework.

The broad pattern is therefore that the primary outcome offers a direct randomized comparison at 18 months, while the secondary outcomes contribute partial information about response and adverse events and do not provide a complete parallel statistical account. None of these summaries, taken alone, settles the broader comparison between treatment strategies.

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

• Overall Survival
• Number of Participants With Complete Response Intensive Chemo-immunotherapy Plus Maintenance or Consolidation Bortezomib
• Number of Participants With Grade 3, 4 or 5 Adverse Event at Least Possibly Related to Treatment.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome summarized at a fixed time point. The registry says that progression-free survival at 18 months was estimated with the Kaplan-Meier method. This method uses the timing of events and follow-up, rather than treating every participant as if their outcome were observed over an identical period. A participant who has not had a recorded event by their last observation may contribute follow-up until that point; this is generally called censoring. The specific censoring rules and follow-up procedures are not reported in the registry record.

What does the Kaplan-Meier estimate represent?

In general, the Kaplan-Meier method estimates the probability of remaining event-free over time while accounting for participants whose event status is not observed through the full follow-up period. At the specified time point, the registry reports the estimate as a percentage. It is therefore a model-based time-to-event estimate, not necessarily the raw proportion calculated by dividing the number without an event by everyone initially assigned to an arm. The registry record does not give the event times, numbers censored, or a survival curve’s underlying risk sets, so those features cannot be independently assessed from the posted summary.

For this endpoint, an event is defined by progression or death, because the outcome is being alive and progression-free. The record does not give the operational definitions of progression, the assessment schedule, or how deaths and progression dates were adjudicated. Those details matter to endpoint reproducibility, but cannot be inferred from the summary description.

How should the between-arm contrast be read?

The posted risk difference is expressed as Arm B relative to Arm A. A difference of zero would represent equal estimated rates; a positive value indicates a higher estimated rate in Arm B. The reported estimate is 0.075, and its confidence interval runs from -0.027 to 0.178. Since the interval crosses zero, it includes the possibility of no difference as well as values in either direction. The interval is a range of values compatible with the data and analysis under the method’s assumptions; it is not a guarantee that the true effect lies within that particular interval.

The recalculated unadjusted p-value is 0.157. A p-value is a probability, calculated under a specified null model, of obtaining results at least as incompatible with that model as the observed results. It is not the probability that the null model is correct, and it does not measure the size or clinical importance of a difference. The registry lists no reported sponsor analysis for this comparison. The recalculated comparison is a simple unadjusted re-calculation from posted summary statistics, so it should not be confused with a model-adjusted analysis or with an analysis plan documented by the investigators.

Why are the confidence intervals useful?

A confidence interval conveys uncertainty around an estimate. In general, a narrower interval reflects greater precision, while a wider interval indicates that the data allow a broader range of values. Arm-specific intervals describe uncertainty in each rate; the interval around the direct contrast addresses uncertainty in the difference between arms. Separate arm intervals should not be used as a substitute for the interval on the contrast, because the uncertainty of a difference depends on both estimates and their statistical relationship.

The confidence intervals are reported as 95% intervals. In general, this confidence level describes the long-run coverage property of the interval procedure under its assumptions, rather than a probability statement about this specific interval after it has been calculated. The registry does not report the exact procedure used to calculate the intervals, so the underlying interval method cannot be checked from the record.

What does randomization contribute?

Random assignment is intended, in general, to make groups comparable with respect to both measured and unmeasured characteristics at the point of assignment. It supports a causal comparison when the assigned strategies are analyzed appropriately and follow-up, outcome measurement, and missingness are handled in ways that preserve the randomized comparison. The registry identifies the trial as randomized and open-label, but the sequence generation and concealment methods are not reported. Open-label status means masking is listed as none; the record does not say how this affected treatment decisions, follow-up, or outcome assessments.

The two arms differ in dose schedule and planned number of cycles, in addition to being described as maintenance and consolidation. Consequently, the contrast represents the assigned strategies as a whole. It cannot isolate the effect of timing, dose, schedule, or duration individually.

What should be understood about secondary analyses?

The registry lists overall survival, complete response, and adverse-event outcomes among the secondary outcomes. Quantitative results and analyses are not posted for all of those outcomes in the record. The complete-response summary has an unadjusted recalculated contrast, but no reported sponsor analysis. Such secondary comparisons are generally less conclusive than a prespecified primary comparison, especially when several outcomes are examined without a reported multiplicity strategy. The registry record does not report whether any adjustment, hierarchy, or other multiplicity control was planned.

No adjusted analyses, subgroup analyses, interim analyses, or detailed statistical analysis plan are reported in the registry record. Their absence from the record should not be taken as evidence that they did or did not occur. The posted summary supports interpretation of the estimates and their uncertainty, but not reconstruction of every analytic decision.

11. Confidence Intervals and Precision

The primary arm estimates are 88.5% for Arm A and 96.0% for Arm B. Their 95% confidence intervals are 80.2% to 97.6% and 90.7% to 100.0%, respectively. The intervals show appreciable uncertainty around each point estimate, particularly for Arm A. The upper bound for Arm B reaches 100.0%; this is an interval limit, not evidence that every participant remained alive and progression-free.

For the direct comparison, the risk difference is 0.075, with a 95% confidence interval from -0.027 to 0.178. This interval includes zero and covers both a possible negative contrast and a possible positive contrast. The point estimate alone is not enough to describe the result: the interval indicates that the precise size and direction of the difference are uncertain. The recalculated unadjusted p-value is 0.157, which is consistent with the interval not excluding zero under the corresponding unadjusted comparison, but the p-value does not replace the interval’s information about the range of estimates.

In general, confidence intervals summarize statistical uncertainty conditional on the data and analysis method; they do not account automatically for every limitation, such as incomplete follow-up, measurement bias, or selective reporting. The registry record does not give the interval calculation details, censoring information, or analysis-population rules. Those missing details constrain assessment of precision beyond the reported intervals.

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 non-time-to-event outcomes, the figures are participants per arm. The general assumptions listed for the planning exercise are a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not descriptions of the probability that the completed trial found an effect. This is not observed power.

The rows that use 100%, 75%, and 50% of the observed effect show how the planning requirement changes when the target difference is smaller than the observed estimate. A smaller effect is generally harder to distinguish from random variation, so more participants are needed to achieve the same target power under the same assumptions. The figures should be read as conditional illustrations, not as a recommendation or as evidence that the trial was intended to detect those particular effects. The registry record does not report whether the original design used these assumptions, an alternative calculation, or another target.

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 = 0.885; treatment proportion p₁ = 0.960; average p̄ = 0.922.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3786 = 0.7420.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3748 = 0.3154.
4. n = (0.7420 + 0.3154)² / (0.0754)² = 196.8, rounded up to 197 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 <- 0.884615384615385                          # control proportion
p1 <- 0.96                          # 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(310037)
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 = 197 (80% power), 263 (90% power)
 75% of observed effect: n per arm = 390 (80% power), 521 (90% power)
 50% of observed effect: n per arm = 963 (80% power), 1,289 (90% power)
power.prop.test: 196.8 
Simulated power at n = 197 per arm: 0.818 (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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the investigators planned an adjustment for multiple statistical tests, a hierarchy among outcomes, or another procedure for controlling multiplicity. This matters because the record lists several secondary outcomes in addition to the primary endpoint. When many outcomes are examined, the chance of observing at least one result that appears unusual by chance can increase. In general, multiplicity methods address that issue by changing the testing or interpretation strategy. Without a reported plan, the recalculated unadjusted p-values should not be read as if they necessarily represent a study-wide error-controlled analysis.

Missing-data handling and analysis populations are also not described in sufficient detail. The registry gives endpoint group sizes for the primary estimates and different group sizes for the complete-response outcome, but it does not explain the differences or state how participants with incomplete outcome information were handled. It does not report whether analyses followed intention-to-treat principles, used a per-protocol population, or applied another population definition. The record also does not describe loss to follow-up, censoring rules, or sensitivity analyses for missing outcomes.

For the primary time-to-event endpoint, appropriate handling of censoring is important because participants may have different observed follow-up. The Kaplan-Meier method is identified, but the registry record does not give the number of participants censored, the timing of censoring, or whether censoring was considered independent of the event process. For the secondary binary outcome, the record does not explain how incomplete response assessments were treated.

No interim analyses, stopping rules, detailed analysis plan, or subgroup analysis plan are reported in the registry record. These omissions limit assessment of whether the posted comparisons reflect all planned analyses and how the investigators intended to address multiplicity or missing information. They should be treated as unreported details, not as proof that a particular procedure was or was not used.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: platelet count decreased (21.2%), hemoglobin decreased (19.2%), neutrophil count decreased (19.2%), lymphocyte count decreased (18.0%), fatigue (15.4%).

The registry reports serious adverse events for 13 of 52 participants in Arm A and 10 of 50 in Arm B. It also reports other adverse events for 52 of 52 in Arm A and 50 of 50 in Arm B. These are the arm-specific counts and denominators recorded for those safety summaries; they are not a comparison adjusted for follow-up time or other factors. The registry lists common serious-event terms, including platelet count decreased, hemoglobin decreased, neutrophil count decreased, lymphocyte count decreased, fatigue, and leukocyte count decreased, with the posted percentages attached to those terms.

The record does not provide a complete event-level breakdown by arm in the summary, so the listed terms should not be assigned to a particular arm. It also does not report death counts in the safety summary. The serious-event counts describe participants with reported serious adverse events, but do not by themselves show event timing, duration, recurrence, or the comparative risk attributable to one strategy. The registry lists adverse events at least possibly related to treatment as a secondary outcome, but these summaries alone do not establish causation.

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

The posted results show that the estimated 18-month progression-free survival rate was higher in Arm B than Arm A. The direct risk-difference estimate is positive, but its confidence interval includes zero and extends in both directions. The statistical summary therefore leaves uncertainty about the size and direction of the underlying contrast. The unadjusted p-value does not resolve that uncertainty or establish the probability that either strategy is better.

This is a randomized comparison of maintenance and consolidation bortezomib in the context of intensive chemo-immunotherapy and autologous stem cell transplantation. It does not compare either strategy with no bortezomib, and the strategies differ in more than their names: the dose schedule, cycle length, and planned number of cycles also differ. Any between-arm contrast applies to the assigned strategies as a whole, not to an isolated component of treatment.

The outcome is an estimated rate at 18 months, not a summary of the entire course of disease or long-term outcome. The registry record lists overall survival as a secondary outcome but does not include a quantitative result for it in the posted information. The available primary result should not be used to infer an overall-survival effect.

Likewise, the result does not establish that the strategies are equivalent or that one is clinically preferable. A finding that the interval includes zero is not proof of equivalence; equivalence requires a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record. The confidence interval also does not account for uncertainties that cannot be evaluated from the record, including analysis-population definitions, censoring details, and missing-data handling.

The most direct interpretation is descriptive: the observed Kaplan-Meier estimates differ, but the posted direct comparison is imprecise. The registry’s endpoint summaries can inform understanding of this particular randomized comparison, but they do not establish a treatment recommendation or guarantee outcomes for patients beyond the trial setting.

17. Why This Trial Matters Statistically

This trial is statistically useful because it compares two active strategies in the same broad treatment sequence. The randomized design supports a direct comparison of maintenance and consolidation bortezomib, while the primary endpoint focuses on a defined time point and incorporates both progression and death. The result illustrates why an arm-specific estimate should be read alongside the confidence interval for the between-arm contrast.

The point estimates alone could suggest a clear separation between strategies. The interval for the difference adds essential context: it includes no difference and allows a range of possible contrasts. That distinction is central to statistical interpretation. A numerical gap between point estimates is not, by itself, evidence that the underlying strategies differ reliably.

The trial also illustrates the importance of distinguishing a primary endpoint from secondary outcomes. Response and adverse-event summaries may add context, but they answer different questions and do not automatically validate the primary comparison. Without a reported multiplicity approach or a full set of analyses, unadjusted secondary findings should be interpreted cautiously.

Finally, the registry record shows how incomplete statistical reporting can limit interpretation even when key estimates are posted. The Kaplan-Meier method is identified, but details about censoring, analysis populations, and missing data are not reported. The trial therefore offers a useful example of both what a randomized estimate can contribute and why transparent reporting of the analysis plan and its implementation matters.

18. 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 registry record does not report the randomization sequence-generation or concealment methods, allocation ratio, or stratification factors. It lists the trial as open-label, but does not describe whether lack of masking could have influenced treatment delivery, outcome assessment, or follow-up. These details limit assessment of how the randomized design was implemented.

The primary endpoint is estimated with Kaplan-Meier methods, but the record does not give event counts, censoring counts, follow-up completeness, censoring rules, or the interval calculation method. It also does not specify the progression criteria or assessment schedule. As a result, the posted 18-month estimate and its uncertainty cannot be independently reconstructed from the registry summary.

The registry enrollment figure differs from the endpoint group sizes, and the complete-response outcome has a different denominator for Arm B than the primary endpoint. The record does not explain those differences or define the analysis populations. This prevents a clear account of which participants contributed to each result and how incomplete data were handled. The reasons for any exclusions or missing assessments are not reported in the registry record.

The original sample-size justification, statistical analysis plan, multiplicity approach, interim analyses, and any stopping rules are not reported. The planning illustrations are based on observed effects and do not establish what the trial was designed to detect. Quantitative results are also not posted for every listed secondary outcome, including overall survival. These reporting limitations mean the available summaries support cautious interpretation of the posted estimates, rather than a comprehensive reconstruction of the trial’s statistical analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bortezomib After Combination Chemotherapy, Rituximab, and an Autologous Stem Cell Transplant in Treating Patients With Mantle Cell Lymphoma — NCT00310037.
• Registry record last updated 2025-10-28; status last verified 2025-10.
• Results first posted 2018-07-31.
• 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.

22. Record Summary

NCT00310037 is a completed randomized phase II trial comparing maintenance and consolidation bortezomib after intensive chemo-immunotherapy and autologous stem cell transplantation for previously untreated mantle cell lymphoma. The registry lists enrollment of 151, no masking, a start date of 2006-06, and primary completion in 2013-12.

The primary outcome is the Kaplan-Meier progression-free survival rate at 18 months. The posted estimates are 88.5% for Arm A and 96.0% for Arm B; the risk-difference interval includes zero. The registry also lists overall survival, complete response, and adverse events as secondary outcomes, but quantitative results and analysis details are incomplete. The record does not report the original sample-size justification, analysis populations, missing-data procedures, or multiplicity plan.