A Study of ASP2215 Versus Salvage Chemotherapy in Patients With Relapsed or Refractory Acute Myeloid Leukemia (AML) With FMS-like Tyrosine Kinase (FLT3) Mutation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of ASP2215 Versus Salvage Chemotherapy in Patients With Relapsed or Refractory Acute Myeloid Leukemia (AML) With FMS-like Tyrosine Kinase (FLT3) Mutation (NCT02421939), a randomized phase 3 study. The primary outcome is Duration of Overall Survival (OS).

2. Clinical Question

This question concerns survival in a specific trial population and compares assignment to gilteritinib with assignment to salvage chemotherapy. The results describe the groups as studied; they do not establish what would happen for every person with AML or for treatment choices outside this trial. The study also assessed remission and other outcomes, but overall survival was the primary endpoint.

3. Trial Design

This was a Phase 3, randomized, open-label, multicenter study with a parallel-group design. The registry record lists 371 participants as enrolled. Of these, 247 were in the gilteritinib group and 124 were in the salvage-chemotherapy group for the primary overall-survival analysis. The primary analysis population was intention-to-treat, defined in the record as all randomized participants.

The study compared gilteritinib with salvage chemotherapy in participants with relapsed or refractory AML and an FLT3 mutation. Gilteritinib was given orally once daily at 120 mg in continuous 28-day cycles. Salvage chemotherapy was given in 28-day cycles; the listed options were low-dose cytarabine, azacitidine, MEC, and FLAG-IDA. Further detail about the regimens is incomplete in the registry record, so the exact chemotherapy received by each participant cannot be described from this record alone.

The study began on 2015-10-20, had primary completion on 2018-09-17, and is listed as completed. The median time of follow-up for overall survival was 17.8 months. The registry record describes the primary outcome as duration of overall survival, from randomization to death from any cause, and gives the Kaplan–Meier method and Greenwood formula for estimating survival and its confidence interval.

Open-label means the study was not masked. The registry record does not report a blinding procedure, the method used to generate or conceal the randomization sequence, or the allocation ratio as a design assumption. The arm counts describe the analyzed groups, but should not be used to infer unreported details of the randomization process. The registry record also does not report the original sample-size justification or the full protocol statistical plan.

4. Participant Flow and Accounting

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

Before assignment: Participants entered the screening period up to 14 days prior to the start of treatment. Prior to randomization, the investigator preselected a salvage chemotherapy for each participant. The randomization was stratified by response to first-line AML therapy and preselected salvage chemotherapy. Treatment was given over continuous 28-day cycles.

Randomization Period: Up to 3 Years

Reasons for not completing this period:

Long Term Follow up: up to 3 Years

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population was the Intention to Treatment (ITT) which consisted of 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.

Population: The analysis population was the Intention to Treatment (ITT), which consisted of all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Duration of Overall Survival (OS), measured over From randomization to until the date of death from any cause (median time of follow-up for OS was 17.8 months).

Overall survival measures the time from randomization until death from any cause. In this study, the registry definition starts the time count on the randomization date and ends it on the date of death. If a participant was not known to have died by the end of follow-up, the observation was censored at the latest date the participant was known to be alive.

Overall survival is used because it is a direct time-to-event outcome: it incorporates both whether death occurred and how long participants were followed before death or censoring. Unlike an outcome limited to a specific cause, death from any cause does not require a judgment about which illness or event caused the death. In general, censoring allows participants with incomplete follow-up to contribute information up to their last known contact, while recognizing that their later survival time is unknown.

The registry record reports median overall survival for each group and a hazard ratio for the comparison. A median describes the point in the estimated survival-time distribution by which half of the group is estimated to have experienced the event. It is not an average survival time, and the median alone does not describe the entire survival pattern. The hazard ratio compares event rates over follow-up under the time-to-event analysis; it is not a ratio of the two reported medians.

The primary outcome is relevant to the study’s stated question about survival, but it does not by itself describe quality of life, treatment burden, or the balance of all possible benefits and harms.

7. Results Posted in the Registry

• Gilteritinib vs Salvage Chemotherapy: hazard ratio 0.64 (95% CI 0.49–0.83), reported p < 0.001 (as reported in the registry).

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.

Duration of Event-Free Survival (EFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Gilteritinib vs Salvage Chemotherapy: hazard ratio 0.79 (95% CI 0.58–1.09), reported p = 0.042 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Gilteritinib vs Salvage Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Complete Remission (CR) Rate

• 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:
  • Salvage Chemotherapy: 10.5% (13/124) versus 21.1% (52/247) on control; risk difference -10.6 percentage points (95% CI -18.0 to -3.2), risk ratio 0.50 (0.28–0.88); unadjusted two-proportion z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Salvage Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Duration of Leukemia-Free Survival (LFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Gilteritinib vs Salvage Chemotherapy: hazard ratio 0.89 (95% CI 0.51–1.56), reported p = 0.665 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Gilteritinib vs Salvage Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several dimensions: event-free survival, remission, leukemia-free survival, duration of remission, transplant, fatigue, and other response measures. They do not all apply to the same participant set or use the same event definition. In general, this breadth can help describe different aspects of the study, but it also means that the results cannot be collapsed into one overall secondary conclusion.

The posted event-free survival and leukemia-free survival comparisons have confidence intervals that are broad, reflecting uncertainty in those estimates. The event-free survival reported p-value is 0.042, while its 95% confidence interval for the hazard ratio ranges from 0.577 to 1.089. The leukemia-free survival comparison has a reported p-value of 0.665 and a 95% confidence interval from 0.506 to 1.563. These measures are not interchangeable with the primary overall-survival endpoint and should be read according to their own definitions and populations.

The complete-remission outcome is a binary response measure, unlike the time-to-event endpoints. The sponsor’s adjusted comparison and the unadjusted re-calculation are distinct analyses, as described in the sponsor reading. The other listed outcomes include measures for which results are not included in the available outcome details; those results are not reported in the registry record presented for analysis.

Secondary results generally carry less weight than a prespecified primary result when many endpoints are assessed. As a general statistical principle, testing multiple outcomes increases the chance of obtaining at least one apparently noteworthy result by chance. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of the secondary tests. Accordingly, individual secondary p-values should be treated as exploratory evidence unless the full analysis plan establishes otherwise. They can add context, but they do not overturn or independently confirm the primary overall-survival result.

The secondary outcome definitions and participant subsets also matter. For example, leukemia-free survival is defined only for participants who achieved CRc, while event-free survival includes relapse, treatment failure, or death. A result in a selected subset cannot automatically be generalized to all randomized participants. The registry record does not report enough detail to characterize every secondary analysis population or missing-data procedure.

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

• Duration of Event-Free Survival (EFS)
• Percentage of Participants With Complete Remission (CR) Rate
• Duration of Leukemia-Free Survival (LFS)
• Duration of Remission
• Percentage of Participants With Composite Complete Remission (CRc Rate)
• Percentage of Participants Who Underwent Hematopoietic Stem Cell Transplant
• Change From Baseline in Brief Fatigue Inventory (BFI)
• Percentage of Participants With Complete Remission (CR) With Partial Hematological Recovery (CRh)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data. Each participant contributes a time from randomization until death or, if death was not known to have occurred, until censoring at the last known contact. Censoring is not the same as recording a death at the censoring date. It marks the point after which the participant’s event status is not known within the available follow-up.

The registry record says that survival rates and 95% confidence intervals were estimated using the Kaplan–Meier method and the Greenwood formula. In general, Kaplan–Meier estimation uses the event and censoring times to estimate the proportion surviving over time. It can use follow-up from participants whose observation ends before the study closes, provided the analysis assumptions are appropriate. The Greenwood formula is a standard way to estimate uncertainty in the Kaplan–Meier survival estimate, which is then used to form a confidence interval.

A median survival time is read from the estimated survival curve at the point where estimated survival reaches one half. It is a summary of the distribution, not a description of every participant’s experience. The registry record reports the median and its 95% confidence interval for each group. The group medians alone do not provide a test of the full survival curves, and a comparison should not be made by dividing one median by the other.

The sponsor’s primary comparison is a hazard ratio estimated with a log-rank method. In general, a hazard is the rate at which an event occurs among participants who have not yet had the event. A hazard ratio compares these rates between groups over follow-up. A value below 1 means the estimated hazard is lower in the first-named group relative to the second under the stated comparison. It is not a direct measure of the absolute difference in survival probability. The interpretation of a single hazard ratio as a stable summary can depend on how the relative hazards behave over time; the registry record does not report an assessment of that assumption.

The reported primary hazard ratio is 0.637, with a 95% confidence interval from 0.490 to 0.830 and p < 0.001. The confidence interval describes the uncertainty around the estimated relative hazard under the analysis. The p-value describes how unusual a result at least this extreme would be under a null model of no difference, assuming the analysis model and test conditions apply. It is not the probability that the null hypothesis is true and does not measure clinical importance.

The record reports median overall survival for 247 participants in the gilteritinib group and 124 in the salvage-chemotherapy group, and defines the primary analysis population as all randomized participants. That intention-to-treat approach compares groups according to random assignment rather than according to treatment received. In general, retaining participants in their assigned groups helps preserve the comparability created by randomization. The registry record does not give a detailed account of treatment changes, adherence, or how every participant’s follow-up was handled beyond its stated censoring definition.

For the complete-remission outcome, the registry record reports percentages by group and a sponsor analysis using the Cochran–Mantel–Haenszel method. In general, this method can estimate a treatment comparison while accounting for defined strata. The registry record does not identify the strata or give enough detail to reconstruct the adjustment. The sponsor-reported adjusted treatment difference was 10.6, with a 95% confidence interval from 2.8 to 18.4 and p = 0.011. A simple unadjusted re-calculation from the posted summary statistics is a different analysis; it should not be substituted for the sponsor’s adjusted result.

For time-to-event secondary outcomes, the record also reports hazard ratios estimated with the log-rank method. The event definitions vary by outcome: event-free survival includes documented relapse, treatment failure, or death, while leukemia-free survival is measured from first CRc until documented relapse or death among participants who achieved CRc. Because the events and analysis populations differ, the hazard ratios and medians for these outcomes answer distinct questions.

General statistical context: over-dispersion matters when observed variation is larger than a model assumes, because standard errors can then be too small and intervals or tests can appear more certain than warranted. The registry record does not describe an over-dispersion assessment for the primary time-to-event analysis. It also does not report a detailed statistical analysis plan, interim analyses, or a multiplicity procedure. These absences limit what can be concluded about unreported analytic choices; they do not alter the numerical results recorded for the primary analysis.

11. Confidence Intervals and Precision

The primary estimate is reported as a hazard ratio of 0.637, with a 95% confidence interval from 0.490 to 0.830. In general, a 95% confidence interval gives a range of values compatible with the data and the estimation procedure at the stated confidence level. It communicates uncertainty about the estimated effect; it is not a range containing 95% of individual participants’ outcomes.

For the primary hazard ratio, the interval lies below 1. This indicates that the range of values compatible with the reported analysis is on the side of a lower estimated hazard for gilteritinib relative to salvage chemotherapy. The interval still spans a range of possible effect sizes, so the single point estimate should not be read as exact. The reported p-value, < 0.001, gives another description of the evidence against the null comparison, but it does not make the estimate precise in every respect or measure the probability that the result will replicate.

The group-specific median estimates also have confidence intervals: 7.7 to 10.7 months for gilteritinib and 4.7 to 7.3 months for salvage chemotherapy. These intervals describe uncertainty in each group’s estimated median. They are not a confidence interval for the difference between medians. A formal comparison of the survival distributions is represented by the reported hazard-ratio analysis, rather than by visually comparing the two median intervals.

Precision depends on the amount and pattern of observed follow-up and events, as well as the analysis method. The registry record reports the number of participants in each primary group and the median follow-up, but does not give the total primary events in the information summarized for this analysis. The confidence interval is therefore important alongside the point estimate: it shows the range of relative hazard values that remain compatible with the reported primary analysis.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations translate an assumed effect into the amount of information that would be needed under stated assumptions. For time-to-event outcomes, the figures are total events across groups, not participants per arm. For the primary overall-survival comparison, the illustration uses 155 total events for 80% power and 207 total events for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 275 and 368 total events, respectively; planning for 50% gives 618 and 827.

For outcomes that are not time-to-event measures, the figures are participants per arm. The assumptions listed for these illustrations 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 trial’s original sample-size assumptions and justification are not reported in the registry record.

In plain terms, 80% power means that, if the assumed effect and planning conditions were true, the design would have an 80% chance of detecting an effect at the chosen significance threshold. The 90% column uses a higher target chance of detection under the same type of assumptions. Neither column guarantees that a study will detect an effect, and neither is a measure of the result’s probability of being true.

Smaller effects require more information to detect reliably. That is why planning for a smaller fraction of the observed effect leads to larger event or participant requirements. These are planning illustrations based on an observed estimate, not the study’s original design calculation, and they are 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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.637, so ln(HR) = -0.4510.
2. d = 4 × (1.96 + 0.842)² / [ln(0.637)]² = 154.4, rounded up to 155 events in total 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
hr <- 0.637                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(2421939)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 155 (80% power), 207 (90% power)
 75% of observed effect: events = 275 (80% power), 368 (90% power)
 50% of observed effect: events = 618 (80% power), 827 (90% power)
Simulated power with 155 events: 0.806 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 232 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 371 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 5.6          # control-arm median, months (converted from the posted unit)
hr          <- 0.637          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 150         p (1-sided)   0.0001
  Events: 70        ~HR at bound   0.4104
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.64   0.0338
   IA 2: 67%                   Z   2.5114
      N: 232         p (1-sided)   0.0060
 Events: 139        ~HR at bound   0.6529
   Month: 24    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.64   0.5603
       Final                   Z   1.9930
      N: 232         p (1-sided)   0.0231
 Events: 209        ~HR at bound   0.7586
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.64   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

For overall survival, the sponsor-reported analysis gives a hazard ratio of 0.637, a 95% confidence interval from 0.490 to 0.830, and p < 0.001 using the log-rank method. The displayed recalculation does not replace that analysis: for time-to-event outcomes, the registry record’s reported hazard ratio is the result to use. The sponsor’s analysis is also the relevant source for the method and comparison as reported.

For complete remission, the sponsor reports an adjusted treatment difference of 10.6, with a 95% confidence interval from 2.8 to 18.4 and p = 0.011, using the Cochran–Mantel–Haenszel method. The unadjusted re-calculation uses posted summary statistics and is not the same estimand or adjustment procedure. It yields p = 0.012. The registry record does not provide the strata or full details needed to reproduce the sponsor’s adjustment. The results should therefore be described as separate analyses, with the sponsor’s own analysis taking precedence when reporting the trial’s analysis.

A re-calculation from summary statistics is useful as a check on the scale and direction of a simple comparison, but it cannot recreate participant-level adjustments or all choices in the trial analysis. The registry record reports no discrepancy for these results. Neither analysis should be represented as a substitute for the original protocol or a complete independent reanalysis.

16. Multiplicity, Missing Data and Analysis Populations

Several secondary outcomes are listed in the registry record, in addition to the primary overall-survival endpoint. When many statistical comparisons are made, the chance of at least one result appearing statistically notable by chance can increase. General approaches to this issue include prespecifying a testing order, adjusting significance thresholds, or treating secondary comparisons as exploratory. The registry record does not report which approach, if any, was used. It therefore does not establish how the secondary p-values should be interpreted as a family of tests.

The record identifies the primary analysis population as intention-to-treat, consisting of all randomized participants. That definition is clear for the primary endpoint, but the record does not report a complete account of analysis populations for every secondary measure. Some outcomes have eligibility conditions in their definitions, such as leukemia-free survival among participants who achieved CRc. Those outcome-specific populations should not be assumed to match the primary population.

For overall survival, the record says participants not known to have died were censored at their last known contact. This explains the stated handling of survival observations without a known death by the end of follow-up. Other missing-data procedures, including how missing assessments were handled for remission, fatigue, or other secondary outcomes, are not reported in the registry record.

The registry record does not report the original sample-size justification, interim analyses, a complete statistical analysis plan, or a multiplicity procedure. It also does not report the randomization-sequence details or an assessment of the proportional-hazards assumption. These details can affect how readers evaluate prespecification, precision, and the interpretation of multiple outcomes. Their absence from the registry record does not demonstrate that a procedure was or was not used; it means that the record does not establish it.

These limits call for a distinction between what is reported and what remains undocumented. The posted primary analysis can be described using its stated population, endpoint definition, method, estimate, interval, and p-value. Broader claims about unreported analysis choices or the certainty of secondary findings cannot be supported by the registry record alone.

17. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (30.9%), pneumonia (17.5%), acute myeloid leukaemia (14.2%), pyrexia (13.8%), sepsis (7.7%).

The posted safety counts use different group sizes from the primary intention-to-treat analysis. For serious adverse events, 246 participants were at risk in the gilteritinib group and 109 in the salvage-chemotherapy group; 211 and 34, respectively, were recorded as affected. For other adverse events, the corresponding at-risk counts were 246 and 109, with 242 and 103 affected. The record also lists 204 deaths in the gilteritinib group and 96 in the salvage-chemotherapy group. These are counts, not adjusted comparisons.

The most frequently listed serious adverse-event terms include febrile neutropenia at 30.9%, pneumonia at 17.5%, acute myeloid leukaemia at 14.2%, pyrexia at 13.8%, sepsis at 7.7%, and acute kidney injury at 7.3%. These percentages describe the reported terms; they do not, by themselves, establish causation or compare risk after accounting for follow-up and group differences.

The registry record does not give enough detail to determine the timing, duration, recurrence, or treatment attribution of each event. Safety counts should therefore be read descriptively alongside the distinct efficacy outcomes, not as a causal assessment based only on the listed totals.

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

The primary analysis reports longer estimated median overall survival in the gilteritinib group than in the salvage-chemotherapy group, alongside a sponsor-reported hazard ratio below 1 and a confidence interval that lies below 1. These results describe the randomized groups in this study and the follow-up captured by the analysis. The confidence interval expresses uncertainty in the relative-hazard estimate; the medians summarize each estimated survival distribution.

The result does not mean that every participant in one group lived longer than every participant in the other, or that an individual’s outcome can be predicted from the group estimate. It does not say that the hazard ratio is a ratio of medians, nor does it quantify an absolute increase in survival time for each participant. The registry record does not provide a basis for making those interpretations.

The comparison is between gilteritinib and a salvage-chemotherapy group that included several listed options. The findings therefore do not isolate a comparison with any one chemotherapy regimen. The record also does not identify whether particular characteristics modify the observed comparison, so subgroup conclusions cannot be drawn from the overall estimate alone.

Overall survival is one important outcome, but it does not capture every consideration relevant to treatment. The posted safety counts and secondary outcomes provide additional context, but they have different definitions, analysis populations, and uncertainties. In particular, the secondary analyses should not be treated as a set of independent confirmations when the registry record does not report a multiplicity plan.

More broadly, statistical evidence is not the same as certainty. The primary p-value does not give the probability that the null hypothesis is true, and statistical significance does not by itself measure clinical importance. The estimates should be read with their confidence intervals, study design, population, follow-up, and the limitations of what is documented in the registry record.

19. Why This Trial Matters Statistically

This trial is statistically informative because it uses random assignment to compare a time-to-event primary outcome between two treatment strategies in a defined population with relapsed or refractory AML and an FLT3 mutation. Randomization is intended, in general, to make treatment groups comparable at assignment and to support a causal comparison of assigned strategies. The primary analysis uses the intention-to-treat population, consistent with comparing groups according to randomization.

The study also illustrates why time-to-event methods are needed. Participants may have different follow-up durations, and some may be alive at their last contact. Kaplan–Meier estimation and censoring allow the analysis to use the observed follow-up without treating a last-contact date as a death. The reported hazard ratio complements the group-specific medians by comparing event hazards over the analyzed period.

The registry results also show why precision and endpoint hierarchy matter. The primary result is accompanied by a confidence interval and a sponsor-reported test, while secondary outcomes address different events and populations. A collection of secondary p-values should not be interpreted as if each were a separately planned primary test, particularly because the registry record does not describe a multiplicity procedure.

Finally, the trial highlights the distinction between a reported analysis and a simple re-calculation from summaries. The sponsor’s adjusted remission analysis and an unadjusted re-calculation answer related but not identical statistical questions. Reporting the method alongside the estimate helps readers understand what the comparison represents and avoids treating all numerical contrasts as interchangeable.

20. 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.

The study was open-label, so participants and study personnel were not masked according to the registry record. For overall survival, the endpoint is death from any cause, but lack of masking may still be relevant to treatment decisions, follow-up, and other outcomes. The registry record does not describe procedures intended to limit such influences.

The comparator was a salvage-chemotherapy group with multiple listed options. The record does not explain how the option was selected or provide sufficient detail to compare outcomes by specific regimen. The group-level comparison should therefore not be interpreted as a separate estimate for each chemotherapy option.

The median overall-survival follow-up was 17.8 months. The estimates characterize the available follow-up and do not establish longer-term patterns beyond what was observed. The registry record does not report the total number of deaths used in the primary analysis summary, nor does it report an assessment of proportional hazards or other diagnostics for the time-to-event analysis.

The record does not report the original sample-size justification, interim analyses, or full statistical analysis plan. It also does not report a multiplicity procedure for the numerous secondary outcomes. These omissions constrain assessment of prespecification and the strength of secondary evidence. The primary analysis is stated to use the intention-to-treat population, but detailed missing-data handling for outcomes other than overall survival is not reported in the registry record.

Finally, the results apply to the enrolled trial population and the study’s treatment strategies. The registry record does not provide evidence to determine whether results differ across patient subgroups or across individual salvage regimens. These limitations do not erase the reported primary estimate, but they narrow the conclusions that can be drawn from it.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of ASP2215 Versus Salvage Chemotherapy in Patients With Relapsed or Refractory Acute Myeloid Leukemia (AML) With FMS-like Tyrosine Kinase (FLT3) Mutation — NCT02421939.
• Registry record last updated 2025-12-04; status last verified 2025-11.
• Results first posted 2019-10-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

NCT02421939 is a completed, randomized, open-label, Phase 3 study comparing gilteritinib with salvage chemotherapy in participants with relapsed or refractory AML with an FLT3 mutation. The registry record lists 371 participants enrolled and identifies overall survival as the primary outcome, analyzed in the intention-to-treat population.

Median overall survival was 9.3 months for gilteritinib and 5.6 months for salvage chemotherapy. The sponsor-reported hazard ratio was 0.637, with a 95% confidence interval from 0.490 to 0.830 and p < 0.001. The analysis used the log-rank method, with survival estimates based on Kaplan–Meier and confidence intervals using the Greenwood formula.

The registry record also lists secondary efficacy and safety outcomes. Their interpretation is limited by differing outcome definitions and populations, and by the absence of reported details on multiplicity, the original sample-size justification, and several analysis procedures.