A Study Comparing Obinutuzumab (RO5072759; GA101) 1000 Milligram (mg) Versus 2000 mg in Participants With Previously Untreated Chronic Lymphocytic Leukemia (CLL) (GAGE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing Obinutuzumab (RO5072759; GA101) 1000 Milligram (mg) Versus 2000 mg in Participants With Previously Untreated Chronic Lymphocytic Leukemia (CLL) (GAGE) (NCT01414205), a randomized phase 2 study. The primary outcome is Objective Response Rate (ORR).

2. Clinical Question

The trial asked whether the objective response rate differed between two obinutuzumab dose regimens in participants with previously untreated chronic lymphocytic leukemia. It compared obinutuzumab 1000 mg with obinutuzumab 2000 mg; it did not compare either dose with placebo or another treatment.

The registry lists 80 enrolled participants, randomized to groups of 41 and 39. The posted response proportions were 48.8% for the 1000 mg group and 66.7% for the 2000 mg group. These observed proportions describe the trial participants; they do not by themselves establish that a dose caused a difference in response.

The response assessment was based on International Workshop on Chronic Lymphocytic Leukemia guidelines. The definition included blood, lymph-node, liver and spleen, blood-cell, and bone-marrow criteria. Response was assessed two months after the last treatment, while the primary outcome timeframe is listed as Week 32. The registry record does not report further detail explaining the relationship between those timing descriptions.

3. Trial Design

This was a randomized, open-label, multicenter, parallel-group Phase II trial. The registry record lists 80 participants as enrolled. Randomization assigned 41 participants to obinutuzumab 1000 mg and 39 to obinutuzumab 2000 mg. Masking was listed as none, so the study was open-label.

Both groups received obinutuzumab by intravenous infusion, with treatment planned for a maximum of 8 cycles. The arm descriptions give a 21 day cycle schedule. For the initial cycle, the 1000 mg regimen split the dose between Day 1 and Day 2; the 2000 mg regimen split it across Day 1, Day 2, and Day 3. Both descriptions list additional doses on Days 8 and 15 of the first cycle and on Day 1 of subsequent cycles through cycle 8. Intravenous corticosteroids were given before the initial dose in both groups.

There is an inconsistency in the cycle length recorded: the brief study summary describes 28-day cycles, whereas the arm descriptions state 21 day cycles. The registry record does not resolve that difference. The arm descriptions provide the more detailed dose schedules, but the cycle-length discrepancy should be kept in mind when interpreting the treatment description.

The primary analysis population was the intent-to-treat population, defined as all randomized participants. The record reports an investigator-assessed response outcome and lists secondary outcomes that include progression-free survival, duration of response, survival, adverse events, and pharmacokinetic measures. The original sample-size justification, the trial’s prespecified statistical analysis plan, and any planned interim analyses are not reported in the registry record. The registry lists the study status as completed.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat population included all randomized participants.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Objective Response Rate (ORR), measured over Week 32.

The primary endpoint was objective response rate at Week 32, expressed as the percentage of participants who achieved a complete response, a complete response with incomplete marrow recovery, or a partial response. The registry record says response was assessed by the investigator according to International Workshop on Chronic Lymphocytic Leukemia guidelines, two months after the last treatment.

The endpoint combines several levels of tumor response into a binary outcome: each participant either met the response definition or did not. Complete response required findings across blood, lymph nodes, liver and spleen, blood counts, and bone marrow. Complete response with incomplete marrow recovery was defined as a complete response with incomplete marrow recovery. Partial response required specified reductions in lymphocyte count, lymphadenopathy, and enlarged liver or spleen, alongside blood-count criteria. The detailed thresholds are set out in the registry’s endpoint definition.

Objective response rate is used to describe how many participants meet a prespecified response definition at an assessment time. It is not a measure of how long response lasts or how long participants remain alive without progression; those are separate outcomes listed among the secondary endpoints. A response proportion also does not convey the full experience of each participant or substitute for outcomes such as safety, duration of response, or survival.

Because this was open-label and the endpoint was investigator-assessed, the assessment was not masked. The registry record does not report additional procedures intended to reduce potential assessment bias. The outcome is therefore best read as the investigator-assessed response proportion recorded for each randomized group, together with the uncertainty around the comparison.

7. Results Posted in the Registry

• Obinutuzumab 2000 mg: 66.7% (26/39) versus 48.8% (20/41) on control; risk difference 17.9 percentage points (95% CI -3.4 to 39.2), risk ratio 1.37 (0.93–2.01); unadjusted two-proportion z-test p = 0.106.

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 Surviving at End-of-Study

• 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:
  • Obinutuzumab 2000 mg: 94.9% (37/39) versus 85.4% (35/41) on control; risk difference 9.5 percentage points (95% CI -3.3 to 22.4), risk ratio 1.11 (0.96–1.29); unadjusted two-proportion z-test p = 0.157.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Obinutuzumab 2000 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning disease control, response duration, survival, adverse events, and pharmacokinetics. These outcomes address aspects of the study that the primary response endpoint does not: for example, progression-free survival and duration of response concern time-related outcomes, while pharmacokinetic measures describe drug exposure. The registry’s outcome inventory therefore indicates a broader set of questions than the primary objective response rate alone.

Among the numerical secondary results described in the registry record, survival at end of study is reported as a count for each group. The record does not provide numerical results in the available outcome details for the other listed secondary outcomes. It is therefore not possible to assess a consistent pattern across all secondary endpoints from the outcome information. The primary response result should not be treated as a proxy for progression-free survival, response duration, safety, or pharmacokinetics.

Secondary outcomes can help place the primary result in context, but their interpretation depends on their definitions, assessment times, analysis methods, and uncertainty. The registry lists 14 secondary outcomes, while only one analysis is listed for the primary comparison and no sponsor analyses are listed for the survival outcome. The original statistical plan, including whether secondary analyses were confirmatory or exploratory, is not reported in the registry record.

When many outcomes are examined, some results may appear notable by chance even if there is no underlying difference. Unless a multiplicity strategy is specified, unadjusted secondary results carry less weight as confirmatory evidence than a prespecified primary analysis. The record does not report whether or how the trial addressed multiplicity. Secondary findings can be descriptive and hypothesis-generating, but they cannot be given the same inferential status as a clearly specified primary comparison without information about the planned analysis and the broader set of tests.

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

• Progression-free Survival (PFS)
• Duration of Response
• Number of Participants Surviving at End-of-Study
• Percentage of Participants With Adverse Events (AE) and Serious Adverse Events (SAE)
• Percentage of Participants With Adverse Events of Interest
• Percentage of Participants With Adverse Events Leading to Study Discontinuation
• PK Parameter: Maximum Serum Concentration (Cmax)
• PK Parameter: Area Under the Serum Concentration-Time Curve Between Dosing Interval Tau (AUCt )

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the response definition or did not. A response rate is the proportion meeting that definition in an assigned group. The posted rates are 48.8% in the 1000 mg group and 66.7% in the 2000 mg group. These are observed group summaries, not estimates adjusted for other participant characteristics.

What does a risk difference describe?

A risk difference compares the response proportions by subtracting one group’s proportion from the other. It is an absolute measure: it describes the difference in probability on the outcome scale, rather than comparing the proportions as a ratio. The unadjusted recalculation reports a risk difference of 0.179 for the 2000 mg group relative to the 1000 mg group. Its confidence interval is -0.034 to 0.392. Values below zero correspond to a lower response proportion in the 2000 mg group, while values above zero correspond to a higher response proportion, under the stated comparison orientation.

The sponsor’s reported method was the Cochran-Mantel-Haenszel method, with a Hauck-Anderson difference. In general, the Cochran-Mantel-Haenszel approach can combine comparisons across strata, rather than treating all participants as one undivided group. The registry record does not identify the strata or give enough analysis detail to reproduce the reported result. The reported estimate is 17.89, with a 95% confidence interval from -4.95 to 40.72. The endpoint is expressed as a percentage, but the registry’s analysis entry does not explicitly state the difference’s scale in its value field.

What does the p-value contribute?

A p-value summarizes how unusual data at least as incompatible with a no-difference model would be if that model and the analysis assumptions held. It is not the chance that a treatment effect exists, and it does not indicate whether a difference matters to patients. The sponsor-reported p-value is 0.078; the unadjusted recalculation gives p = 0.106. These values differ because they refer to different analyses, not because one is a correction of the other. The record does not report the full analysis specification needed to reconcile all methodological choices.

A confidence interval gives a range of values compatible with the data and the method used to calculate it. It reflects sampling uncertainty, not every source of uncertainty. For example, it does not account automatically for open-label assessment, possible missing outcome data, or selective reporting. Both posted intervals include zero, which is consistent with a range of possible differences that includes no difference.

Why can estimates differ across methods?

An unadjusted recalculation uses the group-level event counts and denominators to compare the groups without additional adjustment. A stratified method can produce a different estimate if it accounts for grouping factors, and different statistical procedures can also produce different intervals and p-values. The registry identifies the sponsor’s method but does not report the factors or detailed calculations necessary to verify the precise source of the difference between analyses. The recalculation should thus be understood as a transparent, simple comparison of the posted summaries, while the sponsor-reported result remains the analysis entered in the registry.

The response definition and analysis population also matter. The primary population includes all randomized participants, but the record does not describe how missing Week 32 assessments or other unavailable response data were handled. Missing-data choices can affect a binary response estimate when the outcome is unknown for some participants. The record also does not state whether the analysis used imputation, a missing-equals-nonresponse rule, or another approach. No such method should be assumed.

In general, randomization helps support a comparison of assigned groups by reducing systematic differences at baseline, on average. It does not guarantee balance in a modest-sized trial, and it does not remove uncertainty in the outcome estimate. Open-label treatment assignment and investigator assessment are additional features relevant to interpretation. These design properties do not change the arithmetic of the reported proportions, but they inform how cautiously the estimates should be understood.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for the difference runs from -4.95 to 40.72. The interval includes zero, as well as differences in both directions. Its width indicates that the estimate is not highly precise: the observed data are compatible with a range extending from a modest negative difference to a substantially positive one on the reported scale. The registry does not state a threshold for what size of response-rate difference would be clinically important, so the interval cannot be divided into clinically meaningful and unimportant values using the information in the record.

The unadjusted recalculation has a 95% confidence interval from -0.034 to 0.392. This interval also includes zero and allows for both a negative and positive risk difference. It is on the scale reported by that recalculation and should not be directly substituted for the sponsor’s interval, which comes from a different named method and is recorded on a different-looking numerical scale.

A confidence interval is not a guarantee that the true value lies inside the interval, nor does it describe uncertainty about every aspect of the trial. It quantifies sampling uncertainty under the method’s assumptions. It does not resolve concerns about open-label assessment, missing-data handling, or which of several outcomes should receive emphasis. The registry record does not report all details needed to assess those issues fully.

The group sizes of 41 and 39 and the breadth of the intervals are important context. The trial estimates a possible difference, but the uncertainty remains substantial enough that a range of plausible underlying effects is consistent with the posted results. A point estimate alone would conceal that uncertainty; reading it together with the interval gives a more balanced account of how precisely the response comparison was estimated.

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 sample-size illustration describes hypothetical future planning based on fractions of the observed effect. These entries are participants per arm for 80% power and participants per arm for 90% power; they are not total trial enrollment. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the stated fraction of the observed effect as the difference to detect. These are planning assumptions for the illustration, not the trial’s original design assumptions, which are not reported in the registry record.

For planning for 100% of the observed effect, the illustration gives 119 participants per arm for 80% power and 159 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 215 participants per arm for 80% power and 287 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 488 participants per arm for 80% power and 653 participants per arm for 90% power.

In plain language, 80% power is the planned chance of detecting an effect of the specified size under the planning assumptions if that effect is present; 90% power sets a higher target for that chance. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The figures are illustrations based on the observed estimate, not evidence that the completed trial had a particular probability of finding a difference. This is 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 = 0.488; treatment proportion p₁ = 0.667; average p̄ = 0.577.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6986 = 1.3693.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6871 = 0.5783.
4. n = (1.3693 + 0.5783)² / (0.1789)² = 118.6, rounded up to 119 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 <- 0.48780487804878                          # control proportion
p1 <- 0.666666666666667                          # 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(1414205)
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 = 119 (80% power), 159 (90% power)
 75% of observed effect: n per arm = 215 (80% power), 287 (90% power)
 50% of observed effect: n per arm = 488 (80% power), 653 (90% power)
power.prop.test: 118.6 
Simulated power at n = 119 per arm: 0.808 (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 sponsor-reported primary comparison is a Cochran-Mantel-Haenszel analysis using a Hauck-Anderson difference. It gives an estimate of 17.89, a 95% confidence interval from -4.95 to 40.72, and p = 0.078. This is the statistical analysis entered in the registry record. The registry does not identify the strata used or report the full statistical specification, so that analysis cannot be independently reconstructed in full from the record.

The unadjusted recalculation uses the posted group summaries and gives a risk difference of 0.179, a 95% confidence interval from -0.034 to 0.392, and p = 0.106. It is a simple comparison rather than a reproduction of the sponsor’s named method. Its purpose is to provide a transparent check on the group-level data, not to displace the reported result. The estimates and intervals have different numerical scales as recorded, so they should not be treated as interchangeable entries.

The record marks no discrepancy between the posted summary statistics and the reported analysis. Still, the reported analysis and recalculation answer closely related but not necessarily identical statistical questions because their methods differ. The sponsor’s estimate is the appropriate reference for what the registry reports as its analysis; the recalculation offers additional context about the raw group summaries. Neither result should be interpreted without its interval and the trial’s design limitations.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies objective response rate as the primary outcome and lists multiple secondary outcomes, including progression-free survival, duration of response, survival, several adverse-event outcomes, and pharmacokinetic measures. Evaluating several outcomes creates a multiplicity issue: when many statistical tests are performed, the chance of at least one apparently unusual result can increase even if there is no true difference for any outcome. This general concern is relevant to interpretation, but the registry record does not report a multiplicity adjustment, a hierarchy for testing endpoints, or another strategy for controlling that risk.

The record does not report a complete statistical analysis plan, so it is not clear which secondary analyses were prespecified as confirmatory, which were exploratory, or whether any outcomes were selected for emphasis after results were known. The record also does not report planned interim analyses. These omissions do not show that such procedures were absent; they mean that their use is not reported in the registry record.

The primary population is specified as the intent-to-treat population, including all randomized participants. That definition supports interpreting the primary comparison according to assigned group. However, the registry record does not describe the handling of missing response assessments, participants who discontinued treatment, or other unavailable outcome data. It does not report whether missing outcomes were imputed, counted as nonresponses, excluded from the response calculation, or handled by another method. Missingness and its treatment can affect the response proportions, so this lack of detail limits assessment of the analysis.

The outcome definition is investigator-assessed and the trial was open-label. The registry record does not report masking of outcome assessors or additional safeguards for assessment. The available information therefore supports describing the recorded response rates and reported analysis, but not a full evaluation of every potential source of bias or the trial’s complete inferential plan. The original sample-size justification is also not reported, so the planning illustration should not be mistaken for the rationale used to design this trial.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (5.0%), infusion related reaction (5.0%), neutropenia (2.6%), thrombocytopenia (2.6%), sepsis (2.6%).

The registry reports serious adverse events among 40 participants at risk in the 1000 mg group and 38 participants at risk in the 2000 mg group. Serious adverse events were recorded for 8 participants in each group. The record also reports other adverse events for 40 of 40 participants at risk in the 1000 mg group and 38 of 38 participants at risk in the 2000 mg group. These are descriptive counts as entered in the registry, not adjusted comparisons between groups.

The registry lists febrile neutropenia and infusion related reaction at 5.0% among the top serious adverse event terms, followed by neutropenia, thrombocytopenia, sepsis, and urosepsis at 2.6% each. The record does not specify in these entries whether those terms are pooled across groups or provide group-specific counts for each term. They should not be assigned to a particular dose group based on this information.

Deaths are not reported in the registry record. Counts and percentages for adverse events do not establish that an event was caused by treatment, and descriptive counts alone do not establish a comparative safety difference. The registry information also does not provide the full event-level detail needed to assess timing, duration, severity distribution, or overlap among event categories.

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

The primary data show that the recorded response proportion was higher in the 2000 mg group than in the 1000 mg group. The reported sponsor estimate and the unadjusted recalculation both have confidence intervals that include zero. The results therefore leave substantial uncertainty about the size and direction of the underlying difference. They do not establish that the dose groups differ, and they do not establish that the doses are equivalent.

The trial was designed as a randomized comparison of two dose regimens in previously untreated chronic lymphocytic leukemia. Its results speak most directly to the investigator-assessed objective response outcome at the recorded assessment time and in the participants enrolled. They do not by themselves settle questions about duration of response, progression-free survival, overall survival, pharmacokinetics, or the balance of adverse events. Those are distinct outcomes, and the registry record does not provide enough numerical detail for a full cross-endpoint assessment.

The open-label design and investigator assessment are relevant when interpreting a response endpoint. The registry record does not report whether outcome assessment was masked or how missing response data were handled. These features should be considered alongside the statistical uncertainty, rather than used to claim that the observed difference is either reliable or unreliable by itself.

The findings are not a treatment recommendation. They describe what was observed in this trial and how imprecisely the group comparison was estimated. The record does not establish a clinically important difference threshold, nor does the posted primary result alone determine how the two regimens should be used. Broader clinical judgments require evidence and considerations beyond this registry comparison.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question: how much can be learned from a modest-sized randomized comparison when the observed group proportions differ but the uncertainty interval is broad? The response proportions provide an easily understood absolute summary, while the confidence interval makes clear that the estimate is compatible with a range of possible effects. Reporting both is more informative than focusing only on the point estimate or p-value.

The record also illustrates why the analysis method matters. A straightforward recalculation from group summaries and the sponsor’s named Cochran-Mantel-Haenszel analysis are related but not identical. The registry does not disclose enough detail to reconstruct all features of the latter. Keeping the methods distinct avoids treating an unadjusted calculation as if it were the sponsor’s analysis, while still allowing readers to understand the raw group comparison.

Another statistical lesson is that a trial’s primary endpoint does not summarize all relevant outcomes. Response rate, survival, duration of response, adverse events, and pharmacokinetics address different questions. The registry lists these outcome areas, but the available numerical results are incomplete across them. This makes transparent reporting of outcome definitions, analysis populations, missing-data procedures, and multiplicity strategies important for interpreting the whole evidence base.

Finally, planning illustrations based on an observed effect can show how sample-size requirements change when the target effect is smaller or the desired power is higher. They are not evidence of the completed trial’s power and are not a substitute for the original design justification. The registry record does not report that original justification, so the planning values should be read only as illustrative calculations.

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 trial enrolled 80 participants, split between groups of 41 and 39. The confidence intervals are broad, limiting precision for the primary comparison. The record does not report a clinically meaningful threshold for the response difference, so it is not possible to determine from the registry alone which values in the intervals would be important in practice.

The study was open-label, and the primary endpoint was investigator-assessed. The registry record does not report masked assessment or other safeguards that might address the possibility of assessment bias. The record also does not explain how missing Week 32 assessments were treated. These omissions make it harder to evaluate how robust the response proportions are to assessment and missing-data choices.

The cycle length is described inconsistently: the brief summary states 28-day cycles, while the arm descriptions state 21 day cycles. The record does not resolve this discrepancy. Although dosing days are described, the inconsistent cycle-length information limits clarity about the treatment schedule.

The registry does not report the original sample-size rationale, the complete analysis plan, the multiplicity approach, or planned interim analyses. It also does not identify the strata used in the sponsor-reported Cochran-Mantel-Haenszel comparison. Numerical secondary outcome details are limited in the record, preventing a comprehensive assessment of how the primary finding relates to the full outcome set. These are limitations of the available reporting; they do not establish that a particular procedure was not used.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Comparing Obinutuzumab (RO5072759; GA101) 1000 Milligram (mg) Versus 2000 mg in Participants With Previously Untreated Chronic Lymphocytic Leukemia (CLL) (GAGE) — NCT01414205.
• Registry record last updated 2017-04-17; status last verified 2017-03.
• Results first posted 2014-04-24.
• 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

NCT01414205 is a completed, randomized, open-label, multicenter Phase II trial comparing obinutuzumab 1000 mg with obinutuzumab 2000 mg in participants with previously untreated chronic lymphocytic leukemia. The registry lists 80 enrolled participants and identifies investigator-assessed objective response rate at Week 32 as the primary endpoint.

The observed response proportions were 48.8% for the 1000 mg group and 66.7% for the 2000 mg group. The sponsor-reported difference was 17.89, with a 95% confidence interval from -4.95 to 40.72 and p = 0.078. An unadjusted recalculation from the posted group summaries gives a risk difference of 0.179, with a 95% confidence interval from -0.034 to 0.392 and p = 0.106. Both intervals include zero.

The registry lists secondary outcomes across survival, safety, disease control, and pharmacokinetics, but numerical details are limited for most of those outcomes in the available record. The statistical analysis plan, original sample-size justification, multiplicity approach, missing-data handling, and planned interim analyses are not reported in the registry record.