Bortezomib and Sorafenib Tosylate in Treating Patients With Newly Diagnosed Acute Myeloid Leukemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bortezomib and Sorafenib Tosylate in Treating Patients With Newly Diagnosed Acute Myeloid Leukemia (NCT01371981), a randomized phase 3 study. The primary outcome is Event-free Survival (EFS) for Patients Without High Allelic Ratio FLT3/ITD+ Mutations.

2. Clinical Question

This was a phase III randomized, parallel-arm trial with no masking. The registry record reports enrollment of 1645 across the trial, while the primary endpoint results concern a narrower population and exclude specified groups. The overall enrollment should not be treated as the number contributing to this endpoint: the listed endpoint denominators are 540 for Arm A and 552 for Arm B.

The clinical question is thus narrower than whether the overall study treatment strategy benefits every person enrolled. It asks how the two posted arms compare on a time-to-event outcome in a defined subgroup. The available record does not establish the exact treatment distinction between Arm A and Arm B, nor does it report a formal adjusted comparison. Interpretation should stay within the identified population, endpoint, and registry estimates.

3. Trial Design

The registry identifies this study as a randomized phase III trial using a parallel-group model. It lists no masking. The study concerns newly diagnosed acute myeloid leukemia, and its official title specifies patients with de novo AML and high allelic ratio FLT3/ITD in the trial's broader focus. The primary outcome considered in this analysis, however, is explicitly for patients without high allelic ratio FLT3/ITD+ mutations.

Enrollment was 1645. The registry marks the trial completed. Its recorded start date is 2011-07-06 and its primary completion date is 2019-03-31. These dates describe the record; they do not establish the duration of follow-up for each participant or explain the timing of analyses. Such details are not reported in the registry record.

There are multiple named arms: Arm A, Arm B, three Arm C cohorts, and Arm D. The arm descriptions refer readers to a detailed description rather than stating the assigned treatments. Arm C Cohort 3 is marked as using a different dose, and Arm D may have been reassigned to Arm C. The exact treatment allocation rules, cohort definitions, and dose details are not reported in the registry record's arm descriptions. The registry's intervention list names bortezomib, cytarabine, daunorubicin hydrochloride, etoposide, mitoxantrone hydrochloride, and asparaginase, as well as laboratory biomarker analysis and a pharmacological study. It does not give enough arm-level information to map these interventions to the primary comparison.

The primary endpoint results compare Arm A and Arm B in the stated subgroup. The listed denominators are 540 and 552, respectively. Those numbers differ from overall enrollment because the primary analysis population is restricted and some participants were excluded under the stated eligibility and treatment-start rules. Reasons for all differences between total enrollment and endpoint denominators are not reported in the registry record.

The primary endpoint is an estimated three-year event-free survival percentage, derived using the Kaplan-Meier method. Overall survival and relapse rate in the same mutation-defined population are listed among the secondary outcomes, along with outcomes for Arm C cohorts and toxicity, infection, minimal residual disease, and quality of life measures. The registry lists 25 outcome measures and 15 posted secondary outcomes. The planned sample-size rationale, allocation ratio, stratification factors, concealment procedures, and interim monitoring arrangements 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: Results in the Participant Flow table summarize final (or analysis) arm assignment. Therefore, results for patients on Arms A, B, and D do not include any patient who transferred to Arm C.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Patients ineligible, did not start treatment, or on Arm D are excluded from analyses of EFS. Arm D patients who were not eligible for Arm C by the end of induction I were declared off study per protocol; thus, no outcome data were collected for Arm D patients. Arms A and B are limited to patients without high allelic ratio FLT3/ITD+ mutations.

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Event-free Survival (EFS) for Patients Without High Allelic Ratio FLT3/ITD+ Mutations, measured over Up to 3 years.

The primary endpoint is event-free survival (EFS) for patients without high allelic ratio FLT3/ITD+ mutations, assessed up to 3 years. The registry defines EFS as the time from study entry until the first of induction failure, relapse, secondary malignancy, or death. These events are combined into one time-to-event outcome: an event occurs when any component of the definition is reached.

The registry states that the Kaplan-Meier method will estimate three-year EFS. In general, Kaplan-Meier estimation uses the observed event times and accounts for participants whose event time is not observed through the end of follow-up by treating their follow-up as censored. The registry does not report the number or timing of censored observations, the completeness of follow-up, or details of censoring rules beyond the endpoint definition.

A time-to-event endpoint can use information about when events occur, rather than reducing follow-up to a simple count at one fixed point. That makes it useful when participants have different lengths of observation. The three-year estimate is a summary of the estimated event-free proportion at that time point; it does not describe the full shape of the survival curve or identify which component of the composite endpoint drove the result.

The registry reports Arm A at 45.64% with a 95% confidence interval from 41.34% to 49.83%, and Arm B at 46.95% with a 95% confidence interval from 42.69% to 51.09%. The posted comparison has an unadjusted p-value of 0.651. These are estimates for the specified population, not for all 1645 enrolled participants. A breakdown of endpoint events by component, and further details about the analysis population and follow-up, are not reported in the registry record.

7. Results Posted in the Registry

• Arm B: 46.9% (259/552) versus 45.6% (246/540) on control; risk difference 1.4 percentage points (95% CI -4.5 to 7.3), risk ratio 1.03 (0.91–1.17); unadjusted two-proportion z-test p = 0.651.

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) for Patients Without High Allelic Ratio FLT3/ITD+ Mutations

• 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: 68.5% (378/552) versus 65.0% (351/540) on control; risk difference 3.5 percentage points (95% CI -2.1 to 9.1), risk ratio 1.05 (0.97–1.15); unadjusted two-proportion z-test p = 0.223.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B and the control. The interval gives the range of effects that remain compatible with the data.

Relapse Rate for Patients Without High Allelic Ratio FLT3/ITD+ Mutations

• 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: 46.7% (258/552) versus 46.7% (252/540) on control; risk difference 0.1 percentage points (95% CI -5.8 to 6.0), risk ratio 1.00 (0.88–1.14); unadjusted two-proportion z-test p = 0.981.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Patients Experiencing Grade 3 or Higher Non-hematologic Toxicities and Infections While on Protocol Therapy

• 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: 0.9% (5/575) versus 0.9% (5/559) on control; risk difference -0.0 percentage points (95% CI -1.1 to 1.1), risk ratio 0.97 (0.28–3.34); unadjusted two-proportion z-test p = 0.964.
  • Arm C (Cohort 1): 0.0% (0/12) versus 0.9% (5/559) on control; risk difference -0.9 percentage points (95% CI -1.7 to -0.1); unadjusted two-proportion z-test p = 0.742.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C (Cohort 1) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the clinical picture beyond the primary EFS question. They include overall survival and relapse rate for patients without high allelic ratio FLT3/ITD+ mutations, survival outcomes for the Arm C cohorts, toxicity and infection, minimal residual disease conversion, and parent-reported quality of life. They address distinct questions: an outcome such as overall survival is not interchangeable with the composite EFS measure, while toxicity and quality-of-life outcomes describe different dimensions from disease control.

Across the posted results, the Arm A and Arm B estimates for overall survival are numerically higher in Arm B, while the relapse estimates are very similar. Their unadjusted comparison p-values are 0.223 and 0.981, respectively. The primary EFS comparison likewise has an unadjusted p-value of 0.651. These results do not present a consistent, statistically clear separation between the two arms across the listed outcomes. They should be interpreted as a pattern of estimates and uncertainty, not as proof of no effects.

The toxicity and infection endpoint results include multiple arms and cohorts, some with small denominators. The estimates from the Arm C cohorts are consequently less precise than those from the larger Arm A and Arm B groups. The registry also lists secondary outcomes for which the available result record does not include analyses. No single broad conclusion about all secondary endpoints can be drawn from the outcomes with posted estimates alone.

Secondary results generally carry less weight than a prespecified primary result when their number is large or their analysis plan is unclear. Repeated testing across many outcomes increases the chance that at least one result will appear unusual by chance. The record lists 25 outcome measures and 15 posted secondary outcomes, but does not report a multiplicity strategy, outcome hierarchy, or which secondary analyses were prespecified. The secondary p-values are unadjusted. They are therefore best treated as exploratory signals rather than stand-alone confirmatory evidence.

These secondary outcomes help describe the range of measurements collected, but they do not replace the primary endpoint or resolve its uncertainty. They also cannot be combined informally into a single overall treatment judgment because the outcomes differ in meaning, follow-up, and populations. Formal analyses and their interpretation for the remaining secondary outcomes are not reported in the registry record.

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

• Overall Survival (OS) for Patients Without High Allelic Ratio FLT3/ITD+ Mutations
• OS for Patients on Arm C, Cohort 1
• OS for Patients on Arm C, Cohort 2
• OS for Patients on Arm C, Cohort 3
• Relapse Rate for Patients Without High Allelic Ratio FLT3/ITD+ Mutations
• Proportion of Patients Experiencing Grade 3 or Higher Non-hematologic Toxicities and Infections While on Protocol Therapy
• Proportion of High Risk Children Without HR FLT3/ITD+ Converting From Positive MRD at End of Induction I to Negative MRD at the End of Induction II
• Total Scale Score From Parent-reported Pediatric Quality of Life Inventory Module

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods describe how trial observations are turned into estimates and how much uncertainty surrounds those estimates. In general, the method should fit the outcome type and the way participants are followed. The registry's primary outcome is time-to-event, and it states that Kaplan-Meier estimation is used for three-year EFS. The posted comparison also includes a risk-difference estimate, a confidence interval, and an unadjusted p-value. The registry record does not provide a full statistical analysis plan or explain every computational choice behind the comparison.

What does Kaplan-Meier estimation do?

In general, a Kaplan-Meier curve estimates the probability of remaining event-free over time. It uses the timing of observed events and incorporates participants who leave observation without a recorded event by the time of their last follow-up. Those participants contribute information up to that point and are then treated as censored. This approach is useful when follow-up length varies, but it relies on assumptions about censoring and the observed follow-up. The registry does not report the censoring counts, censoring reasons, or checks of those assumptions.

The reported EFS percentage is an estimate at the stated time point, not a raw proportion calculated by dividing a simple event count by the endpoint denominator. The Kaplan-Meier method can differ from such a raw fraction because it accounts for event timing and censoring. The registry defines which events count for EFS but does not list primary endpoint event counts by type. The result therefore summarizes the combined endpoint without showing the separate contribution of induction failure, relapse, secondary malignancy, or death.

How should the confidence intervals be understood?

In general, a confidence interval is a range of values compatible with the data under a specified statistical procedure. Its width reflects precision: narrower intervals indicate less statistical uncertainty, while wider intervals indicate more. The intervals for the primary arm estimates and for the posted between-arm contrast express uncertainty in different quantities. One interval concerns the estimated EFS in a single arm; the contrast interval concerns the difference between arms.

The posted primary comparison interval includes values on both sides of no difference. This means the data do not tightly locate the contrast on one side of zero. It is not evidence that the true difference is exactly zero. Nor does an interval alone determine whether a difference matters clinically: a threshold for clinical importance is not reported in the registry record.

What does the p-value add?

In general, a p-value summarizes how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The posted primary unadjusted p-value is 0.651. Read alongside the estimate and confidence interval, it indicates that the posted comparison does not provide strong statistical evidence against a no-difference null under the calculation used. The registry does not report a complete specification of that calculation, such as a named test or model.

Unadjusted means that the reported value is not described as corrected for the number of outcomes or comparisons. The distinction matters when a study examines several outcomes, because many tests create more opportunities for a small p-value to arise by chance. Whether any adjustment or hierarchy was prespecified is not reported in the registry record.

Why can over-dispersion matter for other outcome types?

General statistical context: for count or binary outcomes, a model may assume that variability follows a particular distribution. Over-dispersion means the observed variability is greater than the model expects. If it is ignored, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. The primary endpoint is a time-to-event estimate, so this concept should not be used to reinterpret its Kaplan-Meier result. The registry record does not report whether over-dispersion was assessed for any secondary outcome.

What is the role of the posted summary comparisons?

The registry gives arm-level estimates and intervals, plus a risk-difference estimate and interval for the main comparison. In general, the arm-level estimates describe each group, while the contrast directly addresses how far apart the groups are on the chosen scale. The contrast is more informative for a comparative question than visually comparing two separate arm intervals. The posted p-value is unadjusted, and the registry does not report an adjusted treatment-effect model for the primary endpoint.

Several secondary comparisons are also listed, including outcomes with small cohorts. In general, estimates from small groups are especially uncertain, and a point estimate alone can give a misleading impression of stability. Confidence intervals help display that uncertainty. The registry reports wide intervals for several small-cohort safety estimates, and does not report formal analyses for the listed secondary endpoints.

The registry's sample-size illustrations use observed effects and stated planning assumptions. They are not a reconstruction of the trial's original design calculation. A planning illustration translates an assumed effect size and target power into an approximate sample size under a particular statistical framework. It cannot show whether the actual trial was adequately powered for its original objective when that objective and its assumptions are not reported.

Overall, the methods that can be identified are limited: random allocation, parallel arms, no masking, Kaplan-Meier estimation for the primary EFS outcome, and posted unadjusted comparisons. Further details—including the primary analysis model, covariate adjustment, missing-data procedures, multiplicity strategy, interim analyses, and analysis-population definitions beyond the stated exclusions—are not reported in the registry record. Those omissions constrain how fully the posted estimates can be evaluated.

11. Confidence Intervals and Precision

The primary estimates are accompanied by 95% confidence intervals. Arm A's three-year EFS estimate is 45.64%, with an interval from 41.34% to 49.83%. Arm B's estimate is 46.95%, with an interval from 42.69% to 51.09%. The intervals communicate uncertainty about each arm's estimated EFS; they should not be treated as ranges containing a fixed proportion of individual participant outcomes.

For the between-arm comparison, the posted risk-difference interval runs from -0.045 to 0.073. It includes zero, so the data are compatible with no difference as well as with differences in either direction under the method used. The unadjusted p-value is 0.651. These statistics do not establish equivalence, because an equivalence margin and an equivalence-testing analysis are not reported in the registry record.

Precision depends on more than the nominal enrollment. The primary analysis is restricted to a mutation-defined group and excludes certain participants; the registry lists 540 in Arm A and 552 in Arm B for this endpoint. Follow-up length, censoring, and the distribution of event times also affect precision for a time-to-event estimate. Those details are not reported in the registry record, so the effects of follow-up patterns on the intervals cannot be evaluated from the available information.

In general, interval width is a useful companion to an estimate because a similar point estimate can be more or less informative depending on its uncertainty. Here, the contrast interval spans values on both sides of no difference, so the point estimate alone would overstate certainty about the direction and magnitude of the comparison. The registry does not report a clinically important difference threshold, making it impossible to judge precision against such a threshold.

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 illustrations translate an assumed effect into a planning target. For the time-to-event outcomes, the entries are total numbers of events; for the other outcomes, they are participants per arm. The primary EFS illustration is a time-to-event calculation, so its figures refer to total events rather than participants per arm. Other outcome illustrations should be read according to their outcome type, not assumed to use the same unit.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The illustration is computed from the observed effect and is not the trial's own original design calculation; the original sample-size assumptions are not reported in the registry record.

The 80% power column gives the modeled sample-size target for an 80% chance of detecting the assumed effect under those planning assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding target for a 90% chance. These are prospective design concepts: power is the probability of rejecting the null under a specified alternative, not a measure of how likely the observed result is to be true.

Each row changes the effect size used for planning. The rows labeled 100%, 75%, and 50% of the observed effect show targets for progressively smaller assumed effects. Smaller effects are harder to distinguish from random variation, so they require more participants or events to reach the same target power. For example, the primary comparison's planning entries increase from 20,951 total events for 80% power at 100% of the observed effect to 83,715 total events at 50% of that effect. These values are planning illustrations, not numbers of participants or events observed in the trial.

This is not observed power. The illustrations do not show the power achieved by the completed trial, and they do not establish whether the original study design was adequate. That assessment would require the original design assumptions and analysis plan, which are not reported in the registry record.

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 = 0.456; treatment proportion p₁ = 0.469; average p̄ = 0.462.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7051 = 1.3820.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7050 = 0.5934.
4. n = (1.3820 + 0.5934)² / (0.0136)² = 20,950.4, rounded up to 20,951 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 <- 0.455555555555556                          # control proportion
p1 <- 0.469202898550725                          # 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(1371981)
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 = 20,951 (80% power), 28,047 (90% power)
 75% of observed effect: n per arm = 37,227 (80% power), 49,835 (90% power)
 50% of observed effect: n per arm = 83,715 (80% power), 112,070 (90% power)
power.prop.test: 20950.4 
Simulated power at n = 20,951 per arm: 0.796 (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

Multiplicity arises when researchers test or estimate many outcomes, groups, or contrasts. In general, the more comparisons made, the greater the chance that at least one result will look statistically unusual even if no true difference exists. A prespecified primary endpoint helps focus interpretation, while secondary outcomes can add context. However, their inferential weight depends in part on whether the analysis plan anticipated them and whether adjustments or a testing hierarchy were used.

The registry lists 25 outcome measures and 15 secondary outcomes with posted results. The posted primary comparison has an unadjusted p-value, and secondary comparison p-values are also unadjusted. A multiplicity adjustment, gatekeeping procedure, or formal hierarchy for testing outcomes is not reported in the registry record. Without that information, the secondary p-values should not be read as if they each had been protected against the chance of false-positive findings across a large family of tests.

The record does not report interim analyses, stopping boundaries, or whether data monitoring affected the timing of analyses. These are not details that can be inferred from the trial's phase, completion status, or posted p-values. The original statistical analysis plan is not reported in the registry record, so it is unclear which analyses were prespecified and which were added later.

Missing-data handling is also not reported in the registry record. For the time-to-event primary endpoint, the record states the endpoint definition and the use of Kaplan-Meier estimation, but does not report censoring counts, loss-to-follow-up details, or sensitivity analyses. For other outcomes, the handling of missing measurements, incomplete follow-up, or participants who did not contribute an assessment is not reported.

The primary endpoint population has explicit exclusions: patients who were ineligible, did not start treatment, or were on Arm D are excluded. The registry also states that Arm D patients not eligible for Arm C by the end of induction I were declared off study and had no outcome data collected. Other analysis-population definitions—such as whether analyses followed original randomized assignments, how deviations were treated, and how exclusions were applied in each secondary outcome—are not reported in the registry record.

These reporting gaps do not prove that a particular method was or was not used. They mean that the posted results cannot be fully assessed for multiplicity control, missing-data assumptions, interim monitoring, or adherence to a prespecified analysis plan. The most defensible interpretation stays with the estimates and uncertainty that are explicitly reported.

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: death nos (15.2%), hypoxia (9.6%), acute kidney injury (9.1%), hypotension (9.1%), sepsis (8.7%).

The registry reports serious adverse event counts among participants at risk. Arm A has 82 affected participants among 559 at risk, and Arm B has 305 among 575 at risk. The Arm C cohort counts are 6 of 12, 16 of 33, and 30 of 47; Arm D has 2 of 376. These are descriptive counts from the safety record, not adjusted comparisons of risk.

Across the listed serious adverse event terms, the registry gives Death NOS at 15.2%, hypoxia at 9.6%, acute kidney injury at 9.1%, hypotension at 9.1%, sepsis at 8.7%, and left ventricular systolic dysfunction at 8.5%. The record does not provide enough detail in these figures to infer the timing, duration, recurrence, or causal relationship of each event to study treatment. Serious adverse events and the separately listed deaths should not be assumed to be identical categories.

Safety counts can describe what was recorded, but comparisons require caution. The arms and cohorts have different denominators, and some cohorts are small. The registry does not report an adjusted safety analysis or a formal comparison of serious adverse event rates. These counts alone do not establish that an intervention caused an event or that one arm was safer.

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

The posted primary results describe estimated three-year EFS in the trial's defined population without high allelic ratio FLT3/ITD+ mutations. The estimates are 45.64% for Arm A and 46.95% for Arm B, with overlapping 95% confidence intervals. The posted unadjusted comparison does not provide clear statistical evidence of a difference. The risk-difference interval includes zero and extends in both directions, so the result remains compatible with more than one possible underlying contrast.

This finding does not establish that Arm A and Arm B are equivalent. Equivalence requires a prespecified margin and an analysis designed to test whether the difference lies within that margin; neither is reported in the registry record. A nonsignificant p-value is not proof that the treatments have the same effect. Nor does the result establish that either treatment is beneficial or ineffective, because the posted contrast does not compare either arm with a clearly described untreated or standard-care group in the available arm descriptions.

The result also does not apply automatically to all enrolled participants. The primary endpoint concerns a mutation-defined subgroup and excludes participants who were ineligible, did not start treatment, or were in Arm D. The primary results therefore should not be generalized to the entire trial enrollment or to other populations without additional evidence.

EFS is a composite endpoint. A difference or lack of difference in the overall estimate would not by itself tell readers how induction failure, relapse, secondary malignancy, and death behaved separately. The registry does not report primary results broken down by these components. Likewise, secondary outcomes such as overall survival, relapse, toxicity, and quality of life address separate questions and should be read according to their own definitions and uncertainties.

The trial's randomized design is relevant to the comparison, but the registry record does not provide a complete account of allocation procedures, analysis populations, missing-data methods, or the statistical analysis plan. Accordingly, the posted estimates are evidence about the recorded comparison, with limitations in the available reporting. They are not a medical recommendation and do not determine an individual patient's care.

17. Why This Trial Matters Statistically

This trial raises several important statistical issues. First, the primary endpoint is time-to-event rather than a simple event count at a fixed assessment. Kaplan-Meier estimation is designed to incorporate event timing and varying follow-up, but its interpretation depends on follow-up and censoring patterns. The registry states the estimator and endpoint definition but does not report the details needed to evaluate censoring or follow-up completeness.

Second, the primary result applies to a specific mutation-defined population rather than all enrolled participants. The record also specifies exclusions from the primary endpoint analysis. This distinction matters because trial enrollment, randomization, safety denominators, and endpoint denominators describe different populations. Clear population definitions are necessary to understand what each estimate represents.

Third, the comparison illustrates why an estimate should be read alongside its interval. The arm-level EFS estimates are close, but the between-arm interval includes values on both sides of no difference. The unadjusted p-value does not resolve the uncertainty about effect size or clinical importance. The registry does not report a clinical threshold for a meaningful difference or an equivalence framework.

Fourth, the many outcomes raise multiplicity questions. The record lists 25 outcome measures and 15 posted secondary outcomes, but does not report a strategy for controlling false-positive risk across them. The secondary results can provide context, but their unadjusted p-values should not be treated as a set of independent confirmatory tests.

Finally, sample-size illustrations based on observed effects can be useful for understanding how assumed effect size and target power influence planning. They are not the original study-design calculation and are not a measure of power achieved by the completed trial. Distinguishing those concepts prevents retrospective planning figures from being mistaken for evidence that the primary result was adequately powered.

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 available registry record leaves important details unspecified. Although the trial is randomized and parallel-group, the arm descriptions do not identify the assigned treatment regimens. The title and intervention list offer context, but they do not establish which drugs or combinations correspond to Arm A and Arm B. The direct treatment contrast therefore cannot be fully characterized from the arm descriptions.

The primary population is restricted, and its stated exclusions mean that the endpoint denominators are not the same as overall enrollment. The registry does not report a full flow of participants from enrollment through eligibility, treatment start, and endpoint analysis. It also does not report the allocation sequence, concealment, stratification factors, or further details about how randomized assignment was handled in analyses.

For EFS, the record provides the endpoint definition, timeframe, Kaplan-Meier method, and estimates, but not event counts by component, follow-up completeness, censoring patterns, or sensitivity analyses. The absence of these details limits assessment of the assumptions and the clinical interpretation of the composite endpoint.

Statistical reporting is also incomplete. The original sample-size justification, full analysis plan, covariate adjustment, multiplicity approach, interim analysis plan, and missing-data methods are not reported in the registry record. The posted secondary results include unadjusted comparisons, and the available record does not establish which were prespecified. These limitations do not invalidate the reported estimates, but they restrict how thoroughly they can be evaluated and how strongly they should be interpreted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bortezomib and Sorafenib Tosylate in Treating Patients With Newly Diagnosed Acute Myeloid Leukemia — NCT01371981.
• Registry record last updated 2026-06-02; status last verified 2026-05.
• Results first posted 2020-07-07.
• 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

The registry identifies a completed randomized phase III parallel-group trial of 1645 participants with newly diagnosed acute myeloid leukemia. It lists no masking. The primary endpoint is three-year EFS for patients without high allelic ratio FLT3/ITD+ mutations, defined as time to induction failure, relapse, secondary malignancy, or death and estimated using Kaplan-Meier methods.

Three-year EFS is reported as 45.64% for Arm A and 46.95% for Arm B, with 95% confidence intervals of 41.34% to 49.83% and 42.69% to 51.09%, respectively. The posted unadjusted comparison p-value is 0.651. The registry also lists secondary survival, relapse, safety, disease-monitoring, and quality-of-life outcomes, along with serious adverse event counts.

The record does not report the full treatment assignments by arm, original sample-size justification, complete statistical analysis plan, multiplicity strategy, or missing-data procedures. The primary comparison is therefore best understood as a registry-reported estimate for a restricted population, accompanied by uncertainty and limitations in the available methodological detail.