A Study of ASP2215 (Gilteritinib), Administered as Maintenance Therapy Following Induction/Consolidation Therapy for Subjects With FMS-like Tyrosine Kinase 3 (FLT3/ITD) Acute Myeloid Leukemia (AML) in First Complete Remission: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of ASP2215 (Gilteritinib), Administered as Maintenance Therapy Following Induction/Consolidation Therapy for Subjects With FMS-like Tyrosine Kinase 3 (FLT3/ITD) Acute Myeloid Leukemia (AML) in First Complete Remission (NCT02927262), a randomized phase 2 study. The primary outcome is Relapse-free Survival (RFS) Per Independent Review Committee (IRC) Adjudication.

2. Clinical Question

3. Trial Design

This was a phase 2, multicenter, randomized, double-blind, placebo-controlled, parallel-group trial sponsored by Astellas Pharma Global Development, Inc. The registry record identifies it as NCT02927262. It enrolled 98 participants with FLT3/ITD acute myeloid leukemia in first complete remission after induction and consolidation chemotherapy. The study began on 2017-01-10, reached primary completion on 2021-05-25, and is listed as completed.

Participants were assigned to gilteritinib or matching placebo as maintenance therapy. The gilteritinib regimen was 120 mg orally once daily for up to 2 years, subject to protocol-specified discontinuation criteria. The placebo group received matching placebo on the same stated schedule. Randomization and double masking are important design features: random assignment is intended to make the groups comparable on average, while masking can limit differences in care or outcome assessment related to treatment knowledge. The registry record does not report further details about the randomization procedure or how masking was maintained.

The primary outcome analysis included the full analysis set, defined in the record as all randomized participants. There were 63 participants in the gilteritinib group and 35 in the placebo group for this analysis. The registry reports a median time on study drug of 427 days for the gilteritinib group and 212 days for the placebo group. Those treatment-duration summaries do not change the outcome definition or establish why participants stopped treatment.

The trial compared groups on relapse-free survival, with overall survival and event-free survival among the secondary outcomes. The registry also lists change in quantitative minimal residual disease, adverse events, and ECOG performance status. Further details about the original sample-size justification and the study's complete statistical analysis plan 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: Randomization was stratified based on: Age (\<60 or ≥60 years), Geographic region (North America or Europe or rest of the world), Presence of Minimal Residual Disease (MRD) at screening (yes or no), Use of FLT3-inhibiting agents during induction/consolidation (yes or no).

Treatment Period (Up to 744 Days)

Reasons for not completing this period:

Long Term Follow-up (Up to 1201 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) consisted of all participants who were randomized.

5. Baseline Characteristics

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

Population: The full analysis set (FAS) consisted of all participants who were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Relapse-free Survival (RFS) Per Independent Review Committee (IRC) Adjudication, measured over From the date of randomization until the date of documented relapse, or death; (Median time on study drug was 427 days for gilteritinib group and 212 days for placebo group).

Relapse-free survival was the primary endpoint. It measures the time from randomization until documented relapse or death from any cause, whichever occurred first. A time-to-event endpoint retains information about when an event happened, rather than reducing each participant's experience to a simple event or no-event count at a single fixed time. This is useful when participants can be followed for different lengths of time.

The registry defines relapse after complete remission, including remission with incomplete platelet recovery or incomplete hematologic recovery, using specified evidence of leukemia. This includes bone marrow blasts at or above the stated threshold when not attributable to regenerating bone marrow, circulating blasts, or extra-medullary blast foci under the referenced criteria. The record also describes how participants were classified as CRi or CRp. These definitions clarify which clinical events could count as relapse in the endpoint.

The endpoint is used to assess the duration participants remain alive without documented relapse after randomization. Death is included alongside relapse because either event ends relapse-free survival. Kaplan-Meier estimates were used to estimate the survival distribution, and a hazard ratio was reported for the group comparison. The median is the time at which the estimated proportion remaining event-free reaches the midpoint; it is not an average follow-up time. The interpretation of the endpoint depends on event ascertainment, follow-up, and the analysis of participants without a recorded event.

7. Results Posted in the Registry

• Gilteritinib vs Placebo: hazard ratio 0.74 (95% CI 0.41–1.34), reported p = 0.163 (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.

Overall Survival (OS)

• 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 Placebo: hazard ratio 1.13 (95% CI 0.54–2.36), reported p = 0.627 (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 Placebo and the control. The interval gives the range of effects that remain compatible with the data.

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 Placebo: hazard ratio 0.86 (95% CI 0.51–1.46), reported p = 0.296 (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 Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary time-to-event outcomes show a mixed and imprecise pattern rather than a clear, uniform separation across endpoints. Overall survival and event-free survival are related to the primary relapse-free survival question, but they measure different event definitions and should not be treated as duplicate measures. Overall survival concerns death from any cause. Event-free survival includes additional events described in its definition, including relapse, treatment discontinuation, initiation of other anti-leukemic treatment, or death. Those differences mean that the estimates need not match the primary result.

These outcomes can add context about whether the general pattern is consistent across related measures, but they do not independently resolve the uncertainty in the primary comparison. Their confidence intervals are broad, and the registry's p-values do not provide a basis for treating any one secondary finding as definitive. Secondary comparisons are usually interpreted with more caution because examining several outcomes creates more opportunities for an apparently notable result to arise by chance.

The registry also lists change in quantitative minimal residual disease, adverse events, and ECOG performance status among secondary outcomes. Detailed comparative estimates for those measures are not reported in the registry record. Their presence in the outcome list should not be taken to mean that results are available or that they support a particular conclusion.

Whether a multiplicity adjustment or a prespecified sequence of hypothesis tests was used is not reported in the registry record. Without that information, the secondary analyses are best viewed as supportive or exploratory rather than as independent confirmatory evidence. A formal adjustment can change how p-values and intervals are interpreted across a family of outcomes. Even without such an adjustment, the secondary outcomes remain useful for describing what was assessed and for identifying questions that may merit further study, but their inferential weight is lower than that of a prespecified primary endpoint.

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

• Overall Survival (OS)
• Event-Free Survival (EFS)
• Change From Baseline in Quantitative Minimal Residual Disease Measured as Log10-transformed Overall FLT3/ITD Mutation Ratio at Months 3, 6, 12, 24/End of Treatment (EoT)
• Number of Participants With Adverse Events (AE)
• Number of Participants With Eastern Cooperative Oncology Group (ECOG) Performance Status (PS) Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. For each participant, the relevant time starts at randomization and ends at documented relapse or death from any cause, whichever comes first. Participants without a recorded event by their last relevant assessment contribute follow-up up to that point. In general, this is called censoring: the person's event time is not known beyond the time they were last observed, rather than being treated as if an event occurred at that time. The detailed censoring rules and missing-data procedures are not reported in the registry record.

What does a Kaplan-Meier estimate describe?

Kaplan-Meier estimation is a standard way to estimate the proportion of participants who remain free of the endpoint over time while accounting for differing follow-up and censoring. It produces a step-shaped estimate that changes when events occur. The median time is read from that estimated curve at the point where the estimated event-free proportion reaches its midpoint. It is a summary of the curve, not a mean, and it does not describe every point in follow-up. The registry says Kaplan-Meier estimates were used for relapse-free survival.

When event counts are limited or follow-up is incomplete, the estimated curve and its median can be imprecise. A median may be difficult to estimate if the curve does not reach its midpoint during observed follow-up. The registry record reports median estimates for the primary outcome, but does not give the upper confidence limits for those estimates. Consequently, the available median summaries do not provide a complete interval-based description of uncertainty.

What does the hazard ratio summarize?

A hazard is the event rate at a particular time among participants who have not yet experienced the event. A hazard ratio compares the hazards between groups over follow-up. For the primary comparison, the registry reports a hazard ratio of 0.738 for gilteritinib versus placebo. A value below 1 is a point estimate in the direction of a lower event hazard in the gilteritinib group, but the estimate must be read with its confidence interval and the analysis assumptions. It is not a ratio of median survival times, a risk ratio at a fixed time, or a direct statement about an individual participant's outcome.

The registry identifies a Cox proportional hazards model in the endpoint description and reports a log-rank analysis for the group comparison. The Cox model is commonly used to estimate a hazard ratio while accounting for time-to-event follow-up. The proportional hazards framework treats the relative hazards as constant over time for purposes of the model. Whether that assumption was checked, and what diagnostics were used, are not reported in the registry record. The log-rank test compares the observed pattern of events between groups across follow-up under its own assumptions. The registry does not provide further detail on the exact implementation or covariate adjustment.

How should the confidence interval and p-value be read?

A confidence interval gives a range of estimates compatible with the data under the analysis method and its assumptions. Its width indicates precision: a wider interval leaves more uncertainty about the size and potentially the direction of the effect. The primary 95% confidence interval runs from 0.407 to 1.336, so it includes the value 1 that represents equal hazards. That inclusion is consistent with the reported p-value of 0.163. The interval is more informative than a binary label alone because it displays a range of plausible hazard-ratio values.

A p-value evaluates how unusual the observed data, or data more extreme, would be under a specified null hypothesis and statistical model. It is not the chance that the null hypothesis is true, nor the probability that the result occurred by chance in a general sense. It also does not measure the clinical importance of an effect. The reported p-value should be interpreted together with the estimated effect, interval, outcome definition, and study design.

Why can time-to-event results require care?

Time-to-event methods use information about both whether an event occurred and when it occurred. They rely on follow-up being sufficiently well characterized and on appropriate handling of participants whose event status is not known after their last assessment. If censoring is related to the likelihood of an event in ways not accounted for by the analysis, estimates can be affected. The registry record does not provide enough detail to assess that issue or to reconstruct the analysis independently.

Hazard ratios also compress a potentially changing pattern over time into one summary estimate. If the relative hazards vary over time, a single hazard ratio can be harder to interpret as a constant group contrast. No assessment of proportional hazards or alternative time-varying analysis is reported in the registry record. These are general considerations for interpreting a Cox-model estimate, not evidence that an assumption was violated in this trial.

Finally, randomized assignment supports a between-group comparison, but the reported analysis still depends on how participants were followed, how events were adjudicated, and how deviations from assigned treatment were handled. The registry identifies independent review committee adjudication for the primary outcome and defines the full analysis set as all randomized participants. Further detail about adjudication procedures, treatment-policy estimands, and sensitivity analyses is not reported in the registry record.

11. Confidence Intervals and Precision

The reported primary hazard ratio is 0.738, and its 95% confidence interval extends from 0.407 to 1.336. This interval is broad enough to include values on both sides of 1. In statistical terms, it does not distinguish clearly between a lower hazard, little or no relative difference, and a higher hazard under the fitted comparison. The point estimate alone gives a more definite impression than the interval warrants.

The confidence interval reflects sampling uncertainty under the analysis and its assumptions. It does not include every possible source of uncertainty, such as issues arising from missing outcome information, departures from model assumptions, or limitations in how events were recorded. The registry record does not report enough detail to evaluate all of those sources. A 95% confidence interval is not a statement that there is a 95% probability that the true hazard ratio lies in this particular interval; in repeated use, the method is designed to cover the true value at the stated rate under its assumptions.

The median relapse-free survival estimates are 24.02 months for gilteritinib and 15.84 months for placebo. The record reports lower confidence limits of 14.06 months and 3.02 months, respectively, but the corresponding upper limits are not reported in the registry record. The incompleteness of those interval summaries limits what can be said about the precision of each median. Also, confidence intervals around separate medians are not a substitute for an interval around the between-group comparison.

The number of randomized participants was 63 in the gilteritinib group and 35 in the placebo group. The extent of precision for a time-to-event analysis depends importantly on the number and timing of events and on follow-up, not just the number randomized. The total event count for the primary analysis is not reported in the registry record. The reported interval is therefore the most direct summary of uncertainty available for the relative comparison.

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 estimates are expressed as total events for these time-to-event outcomes, not participants per arm. An event is an outcome event relevant to the analysis; the figures should not be read as enrollment targets or as the number of participants actually observed in this trial. The estimates use the observed effect as a reference and also consider planning for 75% or 50% of that observed effect. Those smaller target effects require more events in the planning illustration.

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 the stated fraction of the observed effect. For time-to-event outcomes, the event totals use the Schoenfeld approach. These are planning illustrations based on the observed result, not the trial's original design assumptions; the trial's original sample-size justification is not reported in the registry record.

The 80% power column indicates the estimated total event count under which the planning method would have an 80% chance of detecting the specified effect, if the assumptions held. The 90% power column applies the same interpretation at a higher target chance of detection. Greater target power generally requires more information, and a smaller effect is harder to detect than a larger one, so it requires more events under these assumptions. The estimates are not forecasts of what this particular trial would have found.

This is not observed power. Observed power is not a useful substitute for interpreting the actual estimate and its confidence interval. The trial's evidence is better read from the reported effect estimate, interval, and p-value, while the planning figures illustrate how event requirements change under hypothetical assumptions.

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 = 0.738, so ln(HR) = -0.3038.
2. d = 4 × (1.96 + 0.842)² / [ln(0.738)]² = 340.1, rounded up to 341 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 <- 0.738                              # 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(2927262)
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 = 341 (80% power), 456 (90% power)
 75% of observed effect: events = 605 (80% power), 810 (90% power)
 50% of observed effect: events = 1,361 (80% power), 1,822 (90% power)
Simulated power with 341 events: 0.802 (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 654 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 98 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 <- 15.84          # control-arm median, months (converted from the posted unit)
hr          <- 0.738          # 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: 544         p (1-sided)   0.0001
 Events: 154        ~HR at bound   0.5490
   Month: 20    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.74   0.0338
   IA 2: 67%                   Z   2.5114
      N: 654         p (1-sided)   0.0060
 Events: 307        ~HR at bound   0.7505
   Month: 32    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.74   0.5603
       Final                   Z   1.9930
      N: 654         p (1-sided)   0.0231
 Events: 460        ~HR at bound   0.8303
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.74   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

The registry reports the sponsor's primary log-rank comparison as a hazard ratio of 0.738, with a 95% confidence interval from 0.407 to 1.336 and p = 0.163. These are the reported results used for interpreting the primary comparison. The registry's discrepancy indicator is false, so no discrepancy between the sponsor analysis and a recalculation is indicated.

A recalculated estimate, when available, is a simple unadjusted calculation from posted summary statistics. It cannot reproduce all features of a time-to-event analysis, such as participant-level event timing, censoring, or any analysis details not included in the registry record. For that reason, it should not replace the sponsor's reported analysis. In this case, the sponsor's reported hazard ratio and inference remain the relevant figures to interpret.

The sponsor's p-value is not a measure of the probability that the treatment has no effect. It describes the compatibility of the observed evidence with a specified null comparison under the stated test. The confidence interval is essential context because it shows that the estimate remains uncertain and includes 1. The registry record does not provide further information about covariate adjustment or sensitivity analyses that could clarify how robust the estimate is to analytic choices.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies relapse-free survival as the primary outcome and lists several secondary outcomes, including overall survival, event-free survival, minimal residual disease change, adverse events, and ECOG performance status. Testing multiple outcomes raises a multiplicity issue: as the number of statistical comparisons increases, the chance of at least one nominally unusual result can increase even when no underlying effects are present. General approaches include adjusting the significance threshold, controlling an error rate across outcomes, or using a prespecified testing hierarchy. Whether any such procedure was used is not reported in the registry record.

The registry gives the full analysis set definition for the primary endpoint: all randomized participants. This supports an interpretation based on randomized groups, but the record does not describe how missing outcome assessments, loss to follow-up, treatment discontinuation, or other post-randomization events were handled in the analyses. For a time-to-event outcome, censoring rules matter because they determine how participants without a recorded event contribute follow-up. The registry's outcome timeframe and endpoint definitions do not by themselves specify every analysis rule.

The registry states that Kaplan-Meier estimates and a Cox proportional hazards model were used for relapse-free survival, and reports log-rank analyses for the group comparisons. It does not report whether the proportional hazards assumption was assessed, whether adjusted analyses were conducted, or what sensitivity analyses were performed. The study's full statistical analysis plan, interim analyses, and original sample-size justification are not reported in the registry record. Those absences do not establish that such procedures were or were not used; they limit what can be concluded from the registry description.

These reporting gaps matter because the interpretation of a p-value or confidence interval depends on the planned analysis and the way incomplete follow-up is addressed. They also limit the ability to assess whether secondary findings were intended to be confirmatory. The reported primary result can still be described, but the analysis details available in the registry are not sufficient to reconstruct every decision underlying it.

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: acute myeloid leukaemia recurrent (14.3%), febrile neutropenia (3.2%), hyperleukocytosis (2.9%), neutropenia (2.9%), anal haemorrhage (2.9%).

The registry reports serious adverse events among participants at risk: 24 of 62 in the gilteritinib group and 14 of 35 in the placebo group. The adverse-event risk sets are not identical to the primary outcome analysis counts, which were 63 and 35, respectively. These figures describe the counts recorded in the safety reporting groups; they should not be interpreted as randomized efficacy outcomes or as proof that a particular event was caused by treatment.

Among the listed serious adverse event terms, recurrent acute myeloid leukemia was reported at 14.3%, febrile neutropenia at 3.2%, and hyperleukocytosis, neutropenia, anal haemorrhage, and nausea at 2.9% each. The registry also reports 24 deaths in the gilteritinib group and 12 in the placebo group. The registry record does not establish the causes of those deaths or the time period and definitions used for each count beyond the registry's adverse-event reporting context.

Counts and percentages require attention to their denominators, follow-up, event definitions, and whether participants could contribute more than one event. The registry summary does not provide enough detail to infer comparative risk from these figures alone. They are descriptive safety results and should be read with the trial's full adverse-event reporting, which is not reported in the registry record.

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

The primary result is an estimate of relapse-free survival in the randomized groups, summarized by medians and a hazard ratio. The reported hazard ratio of 0.738 points toward a lower hazard in the gilteritinib group, but the 95% confidence interval from 0.407 to 1.336 includes 1 and the reported p-value is 0.163. The data therefore leave substantial uncertainty about the relative effect. A point estimate in one direction is not the same as a precise or conclusive estimate.

The finding does not establish that gilteritinib improves relapse-free survival, nor does it establish that the groups are equivalent. A non-significant result is not proof of no difference. Equivalence or non-inferiority requires an appropriate design and prespecified margins; such a framework is not reported for this comparison. Conversely, the numerical difference in medians should not be treated as a definitive treatment effect without considering the confidence interval, event pattern, and analysis assumptions.

The result applies to the enrolled study population and the treatment context described in the registry: participants with FLT3/ITD AML in first complete remission after induction and consolidation therapy, randomized to maintenance gilteritinib or placebo. It does not directly answer questions about other populations, treatment settings, regimens, or outcomes. The registry outcome definition includes relapse or death, and a result for this composite endpoint does not identify which component accounts for the observed pattern.

The secondary endpoints can provide context but have their own definitions and uncertainty, and multiplicity handling is not reported. Safety counts are descriptive, with limited details available in the registry summary. Taken together, the posted statistics support a cautious description of an uncertain primary comparison, not a broad claim about benefit, lack of benefit, or safety. Further interpretation would require fuller trial reporting and attention to the design, follow-up, analysis plan, and clinical context.

19. Why This Trial Matters Statistically

This trial is statistically instructive because its randomized, double-blind, placebo-controlled design creates a structured comparison, while the outcome is measured over time. Time-to-event analyses can use information about event timing and accommodate different observed follow-up durations, but they also depend on clear event definitions, appropriate censoring, and model assumptions. The registry identifies several of these elements, including the relapse-free survival definition, Kaplan-Meier estimation, and a reported hazard ratio.

The result also illustrates why effect estimates should be read together with precision. The hazard ratio's point estimate is below 1, yet its confidence interval includes 1 and spans a range that leaves material uncertainty. The p-value alone cannot summarize that uncertainty, and the median estimates do not replace the relative comparison. A complete statistical reading asks what was estimated, how it was estimated, and how much uncertainty remains.

The trial also makes the distinction between a primary outcome and secondary outcomes important. Related outcomes can help describe the pattern, but multiple comparisons and the absence of reported multiplicity procedures limit the strength of inferences from secondary results. Statistical interpretation depends not only on the numerical output but also on prespecification and transparent reporting.

Finally, planning estimates based on an observed effect are not the same as the original trial design rationale or the power actually achieved. The original sample-size justification is not reported in the registry record. Separating hypothetical planning illustrations from observed evidence helps prevent overinterpretation. Together, these features make the trial a useful example of how design, endpoint definition, effect estimation, precision, and reporting completeness work together in biostatistical interpretation.

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 registry record gives a limited account of the statistical methods. It identifies Kaplan-Meier estimation, a Cox proportional hazards model, and log-rank comparisons, but does not report the full analysis plan, model diagnostics, covariate adjustment, or sensitivity analyses. The assumption of proportional hazards and the handling of censoring cannot be assessed from the available description.

The primary median estimates have reported lower confidence limits but no upper confidence limits in the registry record. The total number of primary events and detailed follow-up distribution are not reported, limiting assessment of how much time-to-event information informed the comparison. The treatment-duration summaries differ between groups, but the registry does not explain the reasons for discontinuation or establish how treatment exposure related to outcome follow-up.

The randomized group sizes were unequal, and the placebo group was smaller. This is relevant to precision, although the confidence interval is the direct summary of uncertainty for the reported hazard ratio. The record also reports safety counts in groups at risk that do not exactly match the primary analysis group counts; the summary does not provide further reconciliation or event-level detail.

Multiplicity procedures for secondary outcomes, the original sample-size justification, interim analyses, missing-data rules, and detailed adjudication procedures are not reported in the registry record. The trial is listed as phase 2, and the registry summary does not provide enough information to assess all operational or analytic limitations. These reporting gaps constrain independent evaluation; they should not be mistaken for evidence that a particular procedure was omitted.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of ASP2215 (Gilteritinib), Administered as Maintenance Therapy Following Induction/Consolidation Therapy for Subjects With FMS-like Tyrosine Kinase 3 (FLT3/ITD) Acute Myeloid Leukemia (AML) in First Complete Remission — NCT02927262.
• Registry record last updated 2024-11-26; status last verified 2024-10.
• Results first posted 2022-06-27.
• 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

NCT02927262 was a completed phase 2, randomized, double-blind, placebo-controlled trial of maintenance gilteritinib after induction and consolidation therapy in participants with FLT3/ITD AML in first complete remission. The primary analysis included all randomized participants: 63 assigned to gilteritinib and 35 to placebo. The primary endpoint was relapse-free survival, defined as time from randomization to documented relapse or death from any cause.

The reported median relapse-free survival was 24.02 months with gilteritinib and 15.84 months with placebo. The reported hazard ratio was 0.738, with a 95% confidence interval from 0.407 to 1.336 and p = 0.163. The interval includes 1, leaving uncertainty about the relative comparison. The registry also lists overall survival and event-free survival as secondary outcomes, alongside other measures.

The registry record does not report the original sample-size justification, multiplicity procedure, or full missing-data and model-diagnostic details. Results are best interpreted as an uncertain primary time-to-event comparison, with secondary and safety findings considered in light of the reporting limitations.