A Study to Compare the Efficacy and Safety of a Combined Regimen of Venetoclax and Obinutuzumab Versus Fludarabine, Cyclophosphamide, and Rituximab (FCR)/ Bendamustine And Rituximab (BR) in FIT Patients With Previously Untreated Chronic Lymphocytic Leukemia (CLL) Without DEL (17P) or TP53 Mutation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare the Efficacy and Safety of a Combined Regimen of Venetoclax and Obinutuzumab Versus Fludarabine, Cyclophosphamide, and Rituximab (FCR)/ Bendamustine And Rituximab (BR) in FIT Patients With Previously Untreated Chronic Lymphocytic Leukemia (CLL) Without DEL (17P) or TP53 Mutation (NCT04285567), a randomized phase 3 study. The primary outcome is Minimal Residual Disease (MRD) Response Rate Measured in Peripheral Blood (PB) Using Next Generation Sequencing (NGS).

2. Clinical Question

3. Trial Design

This was a prospective, open-label, multicenter, randomized phase III study with a parallel-group design. The registry lists 166 participants enrolled and describes random assignment in a 1:1 ratio to VEN+G or FCR/BR. The trial status is completed. The recorded study start was 2020-05-28 and the primary completion date was 2024-03-19.

Because the study was open-label and masking was listed as none, treatment assignment was not masked according to the registry. Randomization helps create groups for comparison, while the open-label design means participants and study personnel knew which regimen was assigned. The registry record does not report further details about randomization procedures or any stratification factors.

The primary analysis population was the full analysis set, defined in the record as all randomized participants analyzed according to the treatment to which they were randomized. The primary endpoint was a binary response: whether each participant met the MRD-negative definition in peripheral blood at Month 15. The record lists 80 participants in the VEN+G group and 86 in the FCR/BR group for that endpoint.

The regimens differed in their planned duration and composition. VEN+G comprised 12 cycles of 28 days, with venetoclax starting on Cycle 1, Day 22 after a 5-week ramp-up. The comparator was FCR or BR, described as six cycles. The registry record does not report the original sample-size justification, detailed operational procedures for randomization, or any interim-analysis plan. Such details should not be inferred from the completed enrollment or the posted planning illustrations.

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: Participants were randomized in a 1:1 ratio to receive either venetoclax + obinutuzumab (VEN+G) or fludarabine, cyclophosphamide, and rituximab/bendamustine and rituximab (FCR/BR). All participants in FCR/BR arm were eligible for treatment with BR, whereas only participants ≤ 65 years were eligible for FCR. The choice between FCR or BR was at the investigator's discretion.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all randomized participants, analyzed according to the treatment to which they were randomized.

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: Full Analysis Set (FAS) included all randomized participants, analyzed according to the treatment to which they were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Minimal Residual Disease (MRD) Response Rate Measured in Peripheral Blood (PB) Using Next Generation Sequencing (NGS), measured over At Month 15.

The primary endpoint was the percentage of participants with MRD negativity in peripheral blood (PB) at Month 15. MRD, or minimal residual disease, assesses whether a small amount of CLL remains detectable using a specified measurement method. Here, the registry describes next-generation sequencing (NGS) and defines a negative result as less than 1 CLL cell in 10,000 leukocytes, using a cutoff of less than 10^-4.

This is a binary endpoint: each participant is classified as meeting or not meeting the negativity definition, and the response rate is the percentage meeting it. A rate makes the group-level result interpretable as the frequency of the measured response in each randomized group. It does not describe how long a response lasts or directly measure overall survival. Those are distinct outcomes; progression-free survival is listed separately among the secondary outcomes.

Using a defined assay threshold makes the endpoint operational: the classification depends on the stated specimen, method, and cutoff. The result therefore applies specifically to MRD negativity measured in PB by NGS at the stated time point. The registry says that percentages were rounded to the nearest decimal point. It also specifies that the primary endpoint used the full analysis set, with participants analyzed according to randomized assignment.

MRD is used as a disease-response measure, but a response-rate comparison alone does not establish what that response means for every later outcome. The primary endpoint should be read as a comparison of the proportion meeting this particular laboratory definition at Month 15.

7. Results Posted in the Registry

• Arm B: FCR/BR: 54.7% (47/86) versus 81.2% (65/80) on control; risk difference -26.6 percentage points (95% CI -40.2 to -13.0), risk ratio 0.67 (0.54–0.84); unadjusted two-proportion z-test p = <0.001.

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.

Progression-free Survival (PFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Arm A: VEN+G vs Arm B: FCR/BR: hazard ratio 0.72 (95% CI 0.34–1.54), reported p = 0.400 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Arm A: VEN+G vs Arm B: FCR/BR and the control. The interval gives the range of effects that remain compatible with the data.

MRD Response Rate in PB of FCR/BR Compared With VEN+G at the End of Treatment Response Visit

• 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 B: FCR/BR: 60.5% (52/86) versus 81.2% (65/80) on control; risk difference -20.8 percentage points (95% CI -34.2 to -7.4), risk ratio 0.74 (0.61–0.91); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm B: FCR/BR than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

MRD Response Rate in Bone Marrow (BM) of FCR/BR Compared With VEN+G at the End of Treatment Response Visit

• 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 B: FCR/BR: 38.4% (33/86) versus 70.0% (56/80) on control; risk difference -31.6 percentage points (95% CI -46.0 to -17.3), risk ratio 0.55 (0.40–0.74); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm B: FCR/BR than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary outcomes with posted results, the general pattern is that the MRD response comparisons in peripheral blood and bone marrow favor a higher response rate in the VEN+G group, while the PFS analysis is less conclusive. These outcomes complement the primary PB MRD result, but they are not repetitions of it: they involve a different specimen, assessment timing, or a time-to-event question. The registry’s end-of-treatment PB and BM assessment windows differ between groups, so those secondary responses should be interpreted in their stated timing context.

The PFS estimate is a hazard ratio with a confidence interval that includes the null value, and the reported p-value is 0.400. The record gives a median of 53.3 months for FCR/BR, but a median for VEN+G is not reported in the registry record. This endpoint therefore does not provide the same pattern of evidence as the posted MRD response comparisons. It also addresses a different clinical and statistical question from MRD negativity at a fixed visit.

The registry lists additional secondary outcomes, including objective response, complete response, duration of response, and further MRD response measures. Their presence broadens the outcome coverage, but results for many are not reported in the registry record. The total set of secondary questions also matters statistically: when many outcomes are examined, some may appear noteworthy by chance even if no real effect exists for those outcomes.

Unless an adjustment or a clearly defined testing hierarchy is reported, secondary p-values should be treated as exploratory or supportive rather than carrying the same weight as the primary analysis. The registry record does not report a multiplicity adjustment or testing hierarchy. The secondary findings can add context to the primary result, but should not be used to claim that every outcome differs or that the primary endpoint guarantees a later survival effect.

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

• Progression-free Survival (PFS)
• MRD Response Rate in PB of FCR/BR Compared With VEN+G at the End of Treatment Response Visit
• MRD Response Rate in Bone Marrow (BM) of FCR/BR Compared With VEN+G at the End of Treatment Response Visit
• Objective Response Rate (ORR)
• CR Rate
• MRD Response Rate in PB of Participants With a CR/CRi at the End of Treatment Visit
• MRD Response Rate in BM of Participants With a CR/CRi at the End of Treatment Visit
• Duration of Objective Response (DOR)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports different statistical approaches for the binary response endpoints and the time-to-event endpoint. These methods answer related but distinct questions. The primary endpoint is a comparison of response proportions at a specified assessment, whereas progression-free survival concerns the timing of an event over follow-up.

How should a response-rate difference be read?

A response rate is the proportion of participants meeting the endpoint definition in a group. A risk difference, also called a difference in rates, compares those proportions by subtraction. Its sign depends on the order of the groups: a positive value can indicate a higher rate in the first group when the contrast is written in that order, while reversing the group order reverses the sign. For the primary outcome, the registry reports the sponsor’s difference in rates as 26.60 percentage points for the groups in the reported analysis. The unadjusted recalculation is expressed with FCR/BR relative to VEN+G, so its negative sign describes the same direction of contrast.

The sponsor’s primary analysis used the Cochran-Mantel-Haenszel method. In general, this method can combine comparisons across strata when such strata are part of the analysis. The registry record does not report the strata or further details needed to describe how the method was implemented in this trial. The reported primary result, including its confidence interval and p-value, is therefore best read as the sponsor’s stated analysis rather than as an estimate with unreported adjustments reconstructed from the summary information.

What does a p-value say?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. A small p-value is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The primary analysis reports p < 0.001. The posted response-rate contrast and confidence interval are also important: they describe the direction and range of effect sizes compatible with the analysis. The unadjusted recalculation reports p < 0.001, but it is a simple calculation from posted summary counts rather than the sponsor’s chosen analysis.

How does a hazard ratio differ?

Progression-free survival is a time-to-event outcome. A hazard ratio compares event rates over time under a model-based interpretation; it is not a difference in median survival time or a ratio of response percentages. The registry reports a log-rank analysis and a hazard ratio of 0.72, with a 95% confidence interval from 0.34 to 1.54 and p = 0.400. In general, the null value for a hazard ratio is 1. Because the reported interval includes that value, the result is imprecise about the direction and size of the time-to-event contrast. The posted median is 53.3 months for FCR/BR; the median for VEN+G is not reported in the registry record.

The log-rank method generally compares event-time patterns between groups while accounting for the timing of observed events and censoring. The registry does not report further model details, assumptions checks, or the censoring rules. A hazard ratio should consequently be interpreted alongside the confidence interval and the information about the endpoint and follow-up, rather than as a stand-alone measure.

Why do over-dispersion and model assumptions matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. If a method assumes less variability than is present, its standard errors can be too small and its confidence intervals too narrow. This is a general statistical consideration, not a finding reported for this trial. The registry record does not report an over-dispersion assessment for the primary binary endpoint, nor does it provide enough detail to evaluate model diagnostics. For the posted primary result, the stated method is Cochran-Mantel-Haenszel; no additional model-based assumptions should be attributed to it without registry documentation.

Likewise, a confidence interval has a repeated-sampling interpretation under the assumptions of its method. It is not a guarantee that the true effect lies inside the interval, and it does not account for every possible source of uncertainty, such as missing outcome data or unreported design choices. The registry record does not report detailed missing-data procedures or whether sensitivity analyses addressed those issues.

What does the population definition contribute?

The primary analysis set is described as all randomized participants analyzed according to randomized treatment. This preserves the treatment assignment grouping for the reported comparison. The record does not explain how participants without an evaluable Month 15 PB sample were handled, so the response-rate denominator and missing-result assumptions should not be extended beyond what is explicitly posted. The same caution applies to other endpoints, whose analysis populations and missing-data rules are not fully detailed in the registry information.

These methods distinctions matter: a primary response-rate contrast, a secondary MRD comparison at a different assessment window, and a PFS hazard ratio are not interchangeable estimates. Each should be interpreted with its own endpoint definition, analysis method, uncertainty interval, and reporting completeness.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimated effect. In general, a 95% confidence interval is produced by a method that, under its assumptions and repeated use, would cover the target parameter in 95% of samples. It is not a statement that there is a 95% probability the particular interval contains the true value. Its width indicates how precisely the data estimate the parameter, while its location indicates the range of values compatible with the analysis.

For the primary endpoint, the posted arm-level intervals are 70.97 to 89.11 for VEN+G and 43.55 to 65.42 for FCR/BR. The reported difference in rates is 26.60 percentage points, with a 95% confidence interval from 12.33 to 40.87. This contrast interval is more directly informative about the comparative effect than judging the two separate arm-level intervals alone. Its positive range is consistent with a higher reported response rate in VEN+G under the sponsor’s group ordering.

The unadjusted recalculation gives a risk difference of -0.266, with an interval from -0.402 to -0.130, because it expresses the comparison as FCR/BR relative to VEN+G. The reversed order changes the sign. The recalculation and the sponsor’s reported result should not be treated as identical analyses: the sponsor’s Cochran-Mantel-Haenszel result is the registry’s reported analysis.

Precision varies across endpoints. For PFS, the hazard-ratio interval is 0.34 to 1.54 around an estimate of 0.72, a range that includes the null value for a hazard ratio. This conveys substantial uncertainty about the size and direction of the time-to-event contrast. The record also gives no VEN+G median PFS, limiting what can be said from the posted median summaries.

Confidence intervals describe sampling uncertainty under the method used; they do not resolve questions about missing outcomes, multiplicity, or generalizability. Those require design and analysis details not reported in the registry record.

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 an observed effect, not the trial’s original sample-size justification. The registry record’s original design assumptions are not reported. The stated illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect: 100%, 75%, or 50%.

For the binary response outcomes, entries are participants per arm. For the time-to-event outcome, entries are total events across the study, not participants per arm. The planning table therefore uses different units for the two types of endpoint. Read the endpoint type and unit before comparing any entries.

The 80% power column gives the planning number associated with an 80% chance of detecting the assumed effect under the illustration’s assumptions, if that effect were the true effect and the planning model applied. The 90% power column gives the corresponding number for a 90% chance. Power is a prospective design concept under specified assumptions; the registry’s entries do not describe the probability that this completed study detected its result.

Rows using a smaller fraction of the observed effect require more participants per arm or more total events. For example, the primary endpoint illustration lists 48 participants per arm for 80% power at 100% of the observed effect and 167 participants per arm for 80% power at 50% of the observed effect. These are planning outputs, not observed enrollment requirements or a revised analysis of the trial. The time-to-event illustration uses total events and likewise increases as the assumed effect fraction becomes smaller.

These figures are not observed power. They are conditional illustrations, and their assumptions should not be mistaken for documented choices in the trial’s original design.

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 = 0.812; treatment proportion p₁ = 0.547; average p̄ = 0.680.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6600 = 1.2935.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6326 = 0.5324.
4. n = (1.2935 + 0.5324)² / (-0.2660)² = 47.1, rounded up to 48 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 <- 0.8125                          # control proportion
p1 <- 0.546511627906977                          # 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(4285567)
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 = 48 (80% power), 63 (90% power)
 75% of observed effect: n per arm = 80 (80% power), 107 (90% power)
 50% of observed effect: n per arm = 167 (80% power), 224 (90% power)
power.prop.test: 47.1 
Simulated power at n = 48 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. Analyses Reported by the Sponsor

The primary result reported in the registry is the sponsor’s Cochran-Mantel-Haenszel analysis: difference in rates of 26.60 percentage points, 95% confidence interval 12.33 to 40.87, and p < 0.001. The analysis is labelled as superiority. This is the analysis to use when describing the sponsor’s reported primary finding.

The simple recalculation from the posted primary counts is unadjusted and expresses the risk difference in the opposite group order, FCR/BR relative to VEN+G. Its estimate is -0.266, its 95% confidence interval is -0.402 to -0.130, and its p-value is < 0.001. The sign difference reflects the reversed comparison order; the direction of the contrast is consistent with the posted response rates being higher in VEN+G. The two approaches should not be presented as though they were the same calculation.

The registry record does not report enough detail to reconstruct every element of the sponsor’s analysis. The sponsor’s reported estimate, interval, and p-value take precedence as the official trial analysis. The recalculation is useful as a transparent, unadjusted check based on the posted summary counts, but it does not supersede the reported analysis. The discrepancy flag is false, so no discrepancy between the two analyses is identified in the registry summary.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple endpoints, time points, groups, or statistical comparisons. In general, the more hypotheses examined, the greater the chance that at least one result may appear statistically notable by chance if each is judged without adjustment. Common approaches include adjusting significance thresholds or defining a prespecified hierarchy, but whether either approach was used in this trial is not reported in the registry record.

The registry lists 22 outcome measures and 12 analyses, with 21 secondary outcomes posted in the record summary. The primary endpoint is clearly identified, but a multiplicity-control strategy for secondary outcomes is not reported in the registry record. Accordingly, the secondary p-values should not be interpreted as if they were necessarily protected against the consequences of multiple testing. This does not invalidate the reported values; it limits the strength of confirmatory claims based on secondary comparisons.

Missing-data handling is another important uncertainty. The primary population is described as all randomized participants analyzed according to assigned treatment, but the registry record does not report how participants without an evaluable Month 15 PB measurement were classified or handled. It also does not report the amount or pattern of missing endpoint data, or sensitivity analyses assessing alternative assumptions. Without that information, the effect of missing data on the response-rate estimate cannot be assessed from the registry summary.

The record does not report an interim-analysis plan, stopping rules, or the original sample-size justification. Those design details should not be inferred from the planning illustrations, which are explicitly based on the observed effect and specified assumptions. Further details about analysis populations for individual secondary outcomes, censoring rules for PFS, and model diagnostics are also not reported in the registry record.

These reporting gaps do not change the posted estimates, but they define what can be evaluated. The primary result can be described using the stated analysis, while the completeness of the inferential plan and the robustness of results to missingness or multiple testing remain uncertain.

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: infusion related reaction (11.7%), pyrexia (10.6%), covid-19 (10.4%), covid-19 pneumonia (9.1%), febrile neutropenia (8.2%).

The registry reports serious adverse events for 77 participants at risk in the VEN+G group and 85 at risk in the FCR/BR group. Serious adverse events affected 46 and 42 participants, respectively. The registry also reports other adverse events affecting 76 of 77 participants at risk in VEN+G and 81 of 85 at risk in FCR/BR. Three deaths are listed in each group. These are participant counts and denominators as posted; they should not be converted into comparisons without considering the registry’s definitions and analysis.

The most frequently listed serious adverse-event terms include infusion related reaction, pyrexia, COVID-19, COVID-19 pneumonia, febrile neutropenia, and sepsis. The registry summary does not specify the arm attribution for these listed term percentages, so they should not be assigned to one treatment group. A serious adverse event is a classification based on seriousness criteria, not simply a measure of symptom intensity.

These summaries describe events recorded in the trial, but do not by themselves establish comparative safety. The registry record does not provide the full event-level context, duration, relatedness assessment, or details needed to interpret differences in exposure and risk time. The listed deaths are counts, not an estimate of a causal treatment effect.

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

The primary result describes the proportion of participants meeting a specific MRD-negativity definition in peripheral blood at Month 15. In the posted data, the response rate was higher in the VEN+G group than in the FCR/BR group, and the sponsor’s reported comparison had a 95% confidence interval for the rate difference that did not include zero. This is evidence about that endpoint, at that assessment, in the randomized population described by the registry.

It does not establish that every participant in one group had a better outcome than every participant in the other. A group-level percentage does not reveal an individual’s response, and a confidence interval does not describe the range of individual outcomes. Nor does MRD negativity at a defined visit necessarily answer whether a response persists, whether progression is delayed, or whether survival differs. Those questions require their own outcomes and follow-up.

The secondary PFS result is distinct from the primary MRD result. Its reported hazard-ratio interval includes the null value, and the record does not report a VEN+G median PFS. The secondary MRD results provide additional endpoint-specific information, but multiplicity procedures are not reported. They should therefore be interpreted as supportive context rather than as proof of effects across all outcomes.

The findings apply to the trial population as defined: fit participants with previously untreated CLL requiring treatment and without DEL(17P) or TP53 mutation. They should not automatically be extended to groups outside those criteria. The registry record is not a complete account of all protocol and analysis details; missing-data procedures, the original sample-size justification, and an interim-analysis plan are not reported.

These statistics are not medical advice and do not determine an appropriate treatment for an individual. They describe the posted randomized comparison and its uncertainty, not a guarantee of benefit or harm for a particular person.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition and assessment time matter. The primary outcome is not simply “response”; it is MRD negativity in PB using NGS at Month 15 under a stated threshold. That specificity makes the result interpretable, while also limiting its reach: the result concerns that measurement, specimen, cutoff, and visit rather than every dimension of CLL outcome.

It also shows the value of separating an arm-level response rate from a between-group contrast. The two rates describe how often the measured response occurred in each group; the sponsor’s reported difference and confidence interval directly address the comparative question. Reporting the interval alongside the p-value conveys both the direction and the range of estimates compatible with the analysis, rather than reducing the result to a significance label.

The registry includes both binary response outcomes and a time-to-event outcome. Their estimates cannot be interpreted interchangeably: a difference in response rates is not a hazard ratio, and a hazard ratio is not a difference in medians. The PFS estimate is less precise than the primary result, making it especially important to avoid extending the primary endpoint’s conclusion to survival.

Finally, the available analysis summary has limits. The trial’s own sample-size justification, missing-data handling, multiplicity procedure, and interim-analysis plan are not reported in the registry record. Clear separation of sponsor analyses from simple unadjusted recalculations, and of confirmatory from secondary findings, helps prevent more certainty from being claimed than the record supports.

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 registry summary does not report the original sample-size justification or the assumptions used to plan the trial. The posted planning illustrations are based on the observed effect and therefore should not be read as the study’s original design calculation. Detailed randomization procedures and any stratification factors are also not reported in the registry record.

The primary endpoint’s denominator is described through the full analysis set, but the record does not explain how missing or unevaluable Month 15 samples were handled. The amount of missingness and any sensitivity analyses are not reported. This prevents assessment of how alternative missing-data assumptions might affect the primary response estimate.

The record does not report multiplicity control or a testing hierarchy for the many secondary outcomes, so secondary p-values have limited confirmatory interpretation. The timing of secondary MRD assessments also differs between groups: the posted windows extend to 15 months for VEN+G and 9 months for FCR/BR. These comparisons need to be understood in relation to those different assessment schedules.

For PFS, the registry reports a hazard ratio and one group’s median, but not the VEN+G median. Further details about censoring, model diagnostics, proportional-hazards assessment, and the number of events underlying the estimate are not reported in the registry record. The confidence interval is wide and includes the null value, limiting precision.

The study was open-label with no masking listed, and the registry record does not provide additional details about how that design feature was managed for outcome assessment. The population was restricted to fit participants with previously untreated CLL without DEL(17P) or TP53 mutation; applicability outside those criteria is not established by this comparison. The serious adverse-event summary also lacks full event-level detail and arm attribution for the listed serious-event terms.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare the Efficacy and Safety of a Combined Regimen of Venetoclax and Obinutuzumab Versus Fludarabine, Cyclophosphamide, and Rituximab (FCR)/ Bendamustine And Rituximab (BR) in FIT Patients With Previously Untreated Chronic Lymphocytic Leukemia (CLL) Without DEL (17P) or TP53 Mutation — NCT04285567.
• Registry record last updated 2026-03-03; status last verified 2026-02.
• Results first posted 2025-04-17.
• 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

NCT04285567 is a completed, prospective, open-label, multicenter randomized phase III study comparing VEN+G with FCR/BR in fit participants with previously untreated CLL without DEL(17P) or TP53 mutation. The registry lists 166 enrolled participants and describes a 1:1 allocation. The primary endpoint was the PB MRD-negative response rate measured by NGS at Month 15 in the full analysis set.

The posted primary rates were 81.3% for VEN+G and 54.7% for FCR/BR. The sponsor’s reported difference in rates was 26.60 percentage points, with a 95% confidence interval from 12.33 to 40.87 and p < 0.001. Secondary outcomes include MRD response, PFS, and other response measures. The registry also reports adverse-event counts, but does not report several design and analysis details, including the original sample-size justification, missing-data procedures, and multiplicity strategy.