Blinatumomab in Treating Younger Patients With Relapsed B-cell Acute Lymphoblastic Leukemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Blinatumomab in Treating Younger Patients With Relapsed B-cell Acute Lymphoblastic Leukemia (NCT02101853), a randomized phase 3 study. The primary outcome is Disease Free Survival (DFS) of High-risk (HR) and Intermediate-risk (IR) Relapse Patients.

2. Clinical Question

The registry record frames the study as a comparison of blinatumomab with standard combination chemotherapy in relapsed B-cell acute lymphoblastic leukemia. Its primary endpoint is limited to the high-risk and intermediate-risk randomized cohort, rather than all enrolled participants. The separate low-risk overall-survival result addresses another risk group and a different follow-up period. These distinctions matter: the treatment schedules, risk categories, and endpoint follow-up differ across the comparisons, so the results should not be treated as one pooled estimate for every participant.

3. Trial Design

This was a randomized, parallel-group phase III trial with no masking reported. The registry lists total enrollment of 669 and a start date of 2014-12-17. Primary completion is dated 2021-06-30, and the record status is active, not recruiting. The registry lists the National Cancer Institute as sponsor.

The trial separated participants by relapse-risk group. The primary analysis addressed high-risk and intermediate-risk patients randomized after Induction Block 1 chemotherapy. Those assigned to the control group received Block 2 and Block 3 before allogeneic hematopoietic stem cell transplantation. The blinatumomab group received two 5-week blinatumomab blocks before transplantation. The control arm is marked as closed effective September 18, 2019.

Low-risk participants were assigned to a distinct pair of regimens. The control regimen included Block 2, Block 3, two continuation periods, and maintenance. The blinatumomab regimen included Block 2, blinatumomab cycles, continuation periods, and maintenance. The registry reports overall survival for this risk group over a longer period than the primary endpoint.

The enrollment figure describes the trial as a whole, while the primary endpoint results concern the two high-risk and intermediate-risk groups with 103 and 105 participants, respectively. These denominators should not be confused. Further details of the randomization procedure, allocation concealment, stratification factors, and the original sample-size rationale are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: All patients received 4 weeks of Block 1 reinduction chemotherapy. Following reinduction, individuals in the high- and intermediate-risk group were randomized in a 1:1 ratio to receive Arm A or Arm B, and individuals in the low-risk group were randomized in a 1:1 ratio to receive Arm C or Arm D. Patients who fail Arm A had the option to move to Arm: Blinatumomab salvage therapy

Block 1 Induction

Reasons for not completing this period:

Post Induction Randomization

Reasons for not completing this period:

Blinatumomab Salvage Therapy

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: HR and IR patients randomized per protocol prior to June 30, 2019. This is the cohort of patients who were included in the primary analysis addressing the primary objective on HR/IR patients. Of the total of 216 randomized HR/IR patients, 2 patients with randomization procedure errors and 6 patients randomized after June 30, 2019 were excluded.

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: All relapsed B-ALL patients enrolled on AALL1331

6. Primary Endpoint

The registry lists the primary outcome as Disease Free Survival (DFS) of High-risk (HR) and Intermediate-risk (IR) Relapse Patients, measured over Up to 2 years from date of randomization.

The primary endpoint was disease-free survival for high-risk and intermediate-risk relapse patients, expressed as a percentage of participants. The registry defines disease-free survival as the time from randomization to the first occurrence of treatment failure, relapse, a second malignancy, or death in remission. Participants without a listed event were followed to their date of last contact for the endpoint description. The reported estimates cover up to 2 years from randomization.

Disease-free survival brings several clinically important ways of losing remission or experiencing a subsequent event into a single outcome. This can provide a broader picture than an endpoint based on only one type of event. It also means the endpoint depends on the registry’s composite definition: results do not identify which component accounts for a difference in the combined measure.

The endpoint is time-based, even though the registry displays the results as percentages. In general, time-to-event estimates describe the proportion remaining free of the defined event by a stated follow-up time and can account for participants whose follow-up ends before an event is recorded. The registry states that two-year estimates and two-sided 95% confidence intervals were calculated. The specific estimation procedure and details of how censoring or incomplete follow-up were handled are not reported in the registry record.

7. Results Posted in the Registry

• Arm B (HR and IR Blinatumomab): 54.3% (57/105) versus 38.8% (40/103) on control; risk difference 15.5 percentage points (95% CI 2.1 to 28.8), risk ratio 1.40 (1.04–1.89); unadjusted two-proportion z-test p = 0.026.

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.

Overall Survival (OS) of HR and IR Relapse Patients

• 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 (HR and IR Blinatumomab): 71.4% (75/105) versus 58.3% (60/103) on control; risk difference 13.2 percentage points (95% CI 0.3 to 26.0), risk ratio 1.23 (1.00–1.50); unadjusted two-proportion z-test p = 0.047.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm B (HR and IR Blinatumomab) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Survival (OS) of LR Relapse Patients

• 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 D (LR Blinatumomab): 90.6% (115/127) versus 88.3% (113/128) on control; risk difference 2.3 percentage points (95% CI -5.3 to 9.8), risk ratio 1.03 (0.94–1.12); unadjusted two-proportion z-test p = 0.556.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm D (LR Blinatumomab) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the trial’s results from disease-free survival to overall survival, with separate comparisons for high-risk and intermediate-risk patients and for low-risk patients. This gives a broader view of the posted outcomes, but the comparisons differ in risk group and follow-up period. They should be interpreted as distinct analyses rather than combined into a single overall-survival estimate.

Across the two secondary comparisons, the high-risk and intermediate-risk estimate is numerically more favorable in the blinatumomab group, while the low-risk estimates are close. The uncertainty intervals differ: the high-risk and intermediate-risk comparison has an interval for the unadjusted risk difference just above zero, whereas the low-risk interval includes zero. These patterns are consistent with the general direction of the primary high-risk and intermediate-risk result, but they do not establish a common treatment effect across risk groups.

The secondary endpoints are supportive context, not replacements for the primary endpoint. Overall survival measures a different outcome from disease-free survival, and the two are assessed over different follow-up periods in the risk groups. Different endpoint definitions, follow-up, and group composition mean that concordance or divergence should not be interpreted as a direct replication of the primary comparison.

Unadjusted secondary results carry less weight because the record does not report a multiplicity adjustment or a hierarchy for the secondary tests. When several outcomes are examined, the chance of finding at least one seemingly notable result can increase. The registry also reports no analyses, so the posted comparisons cannot be checked against a documented sponsor analysis plan. These results are best viewed as additional, potentially hypothesis-generating evidence.

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

• Overall Survival (OS) of HR and IR Relapse Patients
• Overall Survival (OS) of LR Relapse Patients

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is a time-to-event measure reported as a percentage at a fixed follow-up point. The registry defines the event as the first of treatment failure, relapse, second malignancy, or death in remission. Time begins at randomization, and the primary endpoint is assessed up to 2 years from that date. The registry says two-sided 95% confidence intervals were calculated for both arms. It does not report the statistical procedure used to estimate those percentages or the exact method used to construct the intervals.

What does a confidence interval describe?

In general, a confidence interval conveys the uncertainty around an estimated quantity under the assumptions of the method used. A narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the value compatible with the data and method. The primary endpoint intervals overlap, but overlap alone is not a formal test of the difference between arms. The posted risk-difference interval is the relevant interval for that contrast; it runs from 0.021 to 0.288.

How should the arm comparison be read?

The posted comparison is a risk difference calculated from summary statistics without adjustment. A risk difference expresses the absolute contrast between two group estimates on the scale used for that calculation. The posted estimate is 0.154. Its interval extends from 0.021 to 0.288, and the unadjusted p-value is 0.026. Because this is a recalculation rather than a reported sponsor analysis, it should not be taken as evidence that the sponsor’s prespecified model or testing procedure produced the same result. The registry record does not provide those analysis details.

General statistical interpretation distinguishes estimation from hypothesis testing. The point estimate gives one value for the contrast; the confidence interval describes uncertainty around that estimate; and a p-value describes how compatible the observed data are with a specified null model under the test’s assumptions. A p-value is not the probability that the null hypothesis is true, and it does not quantify the probability that an observed difference is due to chance in ordinary language.

Why can the endpoint not be treated as a simple event count?

For time-to-event outcomes, participants can have different lengths of observed follow-up. Some may have a recorded event, while others may have no event recorded by their last contact. In general, methods for time-to-event outcomes use the timing of events and account for incomplete follow-up through a censoring framework. The registry describes time from randomization to an event or last contact, but does not report the precise time-to-event method, censoring rules, or checks of method assumptions. The published percentage estimates should therefore be read as the registry’s fixed-time results, not reconstructed from the listed group sizes alone.

What is and is not reported about analysis?

The record lists 11 outcome measures and two posted secondary outcomes, but reports no analyses. It describes a primary population of high-risk and intermediate-risk patients randomized per protocol before June 30, 2019, and identifies this cohort as the one included in the primary analysis addressing the primary objective. The population description also mentions 216 randomized high-risk and intermediate-risk patients and begins to describe exclusions, but the posted wording does not complete that explanation. The exact analysis population and handling of departures from protocol cannot be fully reconstructed from that description.

Important details such as the original statistical analysis plan, the model used for the sponsor’s primary analysis, covariate adjustment, interim analyses, and missing-data procedures are not reported in the registry record. These details can affect how an estimate is interpreted, especially for a time-to-event endpoint. Their absence does not show that no such procedures were used; it means they cannot be evaluated from the registry record.

What does an unadjusted secondary comparison mean?

The two secondary overall-survival comparisons are also recalculated from posted summary statistics, and their p-values are unadjusted. In general, testing several outcomes increases the chance that at least one result appears statistically notable even when there is no underlying difference. A multiplicity strategy may control that risk, but none is reported in the registry record. The secondary p-values should consequently be treated as exploratory evidence, not as if each were the sole prespecified test.

These methods distinctions separate what the registry directly describes from general statistical interpretation. The endpoint definition, follow-up period, reported estimates, intervals, and group sizes are stated in the record. The detailed estimation and analysis procedures that would support a fuller assessment are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is best assessed by reading the confidence interval alongside the point estimate. For the primary endpoint, the control estimate is 39.04%, with a 95% confidence interval from 29.13% to 48.81%. The blinatumomab estimate is 54.44%, with a 95% confidence interval from 44.3% to 63.51%. Each interval spans a range of plausible values under the estimation method, rather than identifying one exact underlying value.

The unadjusted risk-difference interval runs from 0.021 to 0.288. It lies above zero, but its width means the magnitude of the contrast remains uncertain. The estimate should not be treated as an exact, fixed effect. The registry does not report the method used to calculate these intervals, so their assumptions cannot be checked from the record.

The secondary confidence intervals also indicate varying precision across risk groups and outcomes. In general, smaller study groups and fewer observed events can result in less precise estimates, although the registry does not provide event-time details needed to assess that relationship directly for these outcomes. Comparisons between intervals should be interpreted with attention to the different risk groups and follow-up periods, not simply by comparing how wide they look.

Confidence intervals do not address every source of uncertainty. They do not resolve questions about missing data, analysis choices, multiplicity, or how representative the enrolled participants are. Those issues require trial 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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For the binary outcomes in this record, the entries are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study to have 80% power under those assumptions and at the specified effect size. The 90% power column gives the corresponding per-arm planning figure for 90% power. Power is a design probability under a particular assumed effect and statistical model; it is not a measure of how likely the observed result is to be true.

The rows consider planning for 100%, 75%, and 50% of the observed effect. When the effect targeted for detection is smaller, more participants are needed under the same assumptions. This relationship is why the lower-effect planning scenarios have larger sample-size requirements. For instance, the primary-outcome illustration lists 163 participants per arm for 80% power when planning for 100% of the observed effect, and 643 per arm when planning for 50% of the observed effect.

These figures are not observed power. They are hypothetical planning values derived from the observed comparison and should not be read as proof that the trial was adequately or inadequately sized for its original objectives. They also depend on the stated assumptions; differences in allocation, analysis method, follow-up, or target effect could change a real design calculation.

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 = 0.388; treatment proportion p₁ = 0.543; average p̄ = 0.466.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7054 = 1.3826.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6969 = 0.5865.
4. n = (1.3826 + 0.5865)² / (0.1545)² = 162.4, rounded up to 163 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 <- 0.388349514563107                          # control proportion
p1 <- 0.542857142857143                          # 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(2101853)
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 = 163 (80% power), 217 (90% power)
 75% of observed effect: n per arm = 288 (80% power), 385 (90% power)
 50% of observed effect: n per arm = 643 (80% power), 860 (90% power)
power.prop.test: 162.4 
Simulated power at n = 163 per arm: 0.803 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists 11 outcome measures, two posted secondary outcomes, and no reported analyses. It does not describe a multiplicity procedure, a hierarchy among endpoints, or how decisions across multiple tests were controlled. The unadjusted p-values for the primary and secondary recalculated comparisons do not account for the possibility of multiple testing. This limits the strength of conclusions based on isolated p-values, particularly for secondary outcomes.

The primary population is described as high-risk and intermediate-risk patients randomized per protocol before June 30, 2019. The record identifies it as the cohort used for the primary objective and states that 216 high-risk and intermediate-risk patients were randomized. Its description of exclusions mentions 2 patients with randomization procedure errors and 6 patients, but the posted wording does not complete the explanation. The exact relationship between that full randomized group and the endpoint denominators cannot be fully determined from the registry text.

Details of missing-data handling, loss to follow-up, censoring rules, and the treatment of protocol deviations are not reported in the registry record. These are relevant for interpreting a time-to-event endpoint because the outcome is defined from randomization to an event or last contact. The record also does not describe the sponsor’s analysis population in enough detail to establish whether all randomized participants were analyzed according to their randomized groups.

The trial’s original statistical analysis plan, planned interim analyses, sample-size justification, and prespecified adjustment strategy are not reported in the registry record. This does not establish that such plans or procedures did not exist; it limits what can be verified from the posted information. The unadjusted calculations should therefore be distinguished from a complete, prespecified trial analysis.

15. 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 0% 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 (22.2%), hypokalemia (18.5%), alanine aminotransferase increased (14.8%), cytokine release syndrome (11.1%), hypophosphatemia (11.1%).

The registry lists serious adverse event information for several treatment groups and phases, including induction, the high-risk and intermediate-risk arms, the low-risk arms, and blinatumomab salvage therapy. Each entry gives the number at risk and the number affected for serious adverse events, other adverse events, and deaths. For example, the high-risk and intermediate-risk control group lists 26 participants affected by serious adverse events among 109 at risk, while the blinatumomab group lists 45 among 107 at risk. These are counts, not newly calculated percentages.

The listed groups represent different treatment contexts and are not all direct randomized comparisons. The record does not explain overlap between groups or provide exposure-adjusted comparisons, event timing, severity detail for all events, or an attribution method. Death counts are listed, but the registry information presented does not establish that each death was caused by treatment. The serious adverse event terms appearing most often include febrile neutropenia, hypokalemia, increased alanine aminotransferase, cytokine release syndrome, hypophosphatemia, and sepsis. These posted safety summaries describe reported events; they do not by themselves establish comparative safety or causality.

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

The registry results show a higher posted disease-free survival estimate in the blinatumomab group than in the control group for the primary high-risk and intermediate-risk population. The unadjusted recalculated risk-difference interval is above zero, while its width leaves uncertainty about the magnitude of the contrast. This is a statistical description of the posted data, not a complete assessment of the sponsor’s analysis or of all evidence relevant to treatment decisions.

The result applies to the specified risk group, treatment schedules, endpoint definition, and follow-up period. It should not be generalized automatically to low-risk patients, all younger patients with relapsed disease, other treatment settings, or outcomes that were not reported. The low-risk overall-survival result is a separate comparison and cannot be substituted for the primary endpoint.

A confidence interval describes uncertainty under an analysis method; it does not guarantee that the true effect falls within the interval. An unadjusted p-value also does not show the probability that a treatment is effective or that a result is due to chance. The absence of a reported multiplicity plan and sponsor analysis details further limits how strongly the recalculated comparisons can be interpreted.

Nor do these results show which component of the composite disease-free survival endpoint accounts for the observed group estimates. The registry does not provide sufficient detail to determine how missing follow-up or protocol deviations were handled. The findings are therefore best understood as the posted estimates for the registry-defined populations, with important uncertainty about analysis details and the broader interpretation.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates patients by relapse-risk group and evaluates different treatment strategies within those groups. That design makes the target population for each result essential to interpretation. The primary endpoint concerns high-risk and intermediate-risk patients, while low-risk patients have a distinct overall-survival comparison. Keeping these populations separate avoids treating clinically and analytically different comparisons as interchangeable.

The primary outcome also illustrates the value and limitation of a composite time-to-event endpoint. Combining treatment failure, relapse, second malignancy, and death in remission can capture several important events, but a single estimate does not reveal which component drives the result. Component-specific reporting would be needed to assess that question, and it is not included in the registry information.

The record also offers a useful reminder that a point estimate and p-value are not enough to judge precision. The interval for the primary contrast conveys a range of uncertainty, and its width matters alongside whether it includes zero. The planning illustrations further show, under their stated assumptions, that targeting a smaller effect requires more participants per arm. They are planning scenarios rather than evidence about the trial’s original design.

Finally, the record demonstrates why statistical transparency matters. The endpoint definition and group estimates are available, but key details about the analysis plan, missing data, multiplicity, and original sample-size rationale are not reported. Those omissions constrain the extent to which the posted calculations can be treated as a complete account of the trial’s statistical evidence.

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 sponsor’s statistical analysis plan, the method used to estimate the time-to-event percentages, or the detailed method for the confidence intervals. The comparisons discussed are unadjusted recalculations from posted summary statistics, and the record lists no reported analyses. They should not be assumed to reproduce a prespecified sponsor analysis.

The primary population description is incomplete: it identifies a per-protocol high-risk and intermediate-risk cohort randomized before June 30, 2019, and mentions exclusions after stating that 216 patients were randomized, but does not finish describing those exclusions. This prevents a full reconciliation of the stated cohort with the endpoint group sizes. Missing-data handling, censoring rules, and treatment of protocol deviations are also not reported.

The registry reports multiple outcomes but no multiplicity plan. The two posted secondary comparisons are therefore subject to the limitations of unadjusted testing and should not be treated as equivalent in evidential strength to a single primary test. The original sample-size justification and any interim analyses are not reported, so the planning illustrations cannot be used to infer the trial’s design assumptions.

Safety information is presented across treatment groups and phases, without details sufficient to determine group overlap, exposure time, event attribution, or a comparable treatment-emergent risk contrast. The record also does not provide component-specific results for the composite primary endpoint. These limitations concern what can be concluded from the registry record; they do not establish that additional analyses or information do not exist elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Blinatumomab in Treating Younger Patients With Relapsed B-cell Acute Lymphoblastic Leukemia — NCT02101853.
• Registry record last updated 2026-10-21; status last verified 2026-09.
• Results first posted 2022-12-06.
• 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

NCT02101853 is a randomized, parallel-group phase III trial of blinatumomab-based and chemotherapy-based regimens for younger patients with relapsed B-cell acute lymphoblastic leukemia. The registry lists enrollment of 669, a start date of 2014-12-17, primary completion on 2021-06-30, and status active, not recruiting.

The primary outcome is disease-free survival up to 2 years from randomization in high-risk and intermediate-risk patients. The posted estimates are 39.04% for control and 54.44% for blinatumomab. The unadjusted recalculated risk difference is 0.154, with a 95% confidence interval from 0.021 to 0.288 and p = 0.026. Two secondary overall-survival outcomes and adverse-event summaries are also posted.

The registry does not report the sponsor’s analysis details, missing-data procedures, multiplicity approach, or original sample-size rationale. The recalculated comparisons and planning illustrations should be interpreted with those limits in mind.