Efficacy and Safety of Decitabine as Epigenetic Priming With Induction Chemotherapy in Pediatric Acute Myelogenous Leukemia (AML) Subjects: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Decitabine as Epigenetic Priming With Induction Chemotherapy in Pediatric Acute Myelogenous Leukemia (AML) Subjects (NCT01177540), a randomized phase 2 study. The primary outcome is Percentage of Participants With Morphologic Complete Remission (CR).

2. Clinical Question

The registry record also describes broader objectives: activity assessed through complete remission, leukemia-free survival, overall survival, and minimal residual disease, as well as safety and pharmacokinetics of decitabine in pediatric patients. The primary endpoint is a time-specific response measure, rather than a measure of long-term survival. The listed secondary outcomes include DNA methylation, survival, minimal residual disease, and recovery times. Numerical results for those secondary outcomes are not reported in the registry record.

3. Trial Design

This was a randomized, open-label, multicenter, parallel-group phase 2 study in pediatric acute myelogenous leukemia. Participants were assigned to Treatment A, decitabine plus induction chemotherapy, or Treatment B, induction chemotherapy only. The induction regimen is described in the study summary as daunorubicin, cytarabine, and etoposide. The record lists 25 enrolled participants and reports the study status as terminated. The start date was 2011-03-03, and the primary completion date was 2013-07-19.

The study was open label, so treatment masking was not used. The registry record does not give details of the randomization sequence, allocation concealment, stratification, or reasons for termination. It also does not report the planned enrollment target, the original sample-size justification, or the protocol's statistical analysis plan. The listed arm descriptions are blank, although the arm titles identify the treatment groups.

The primary endpoint was the percentage of participants with morphologic complete remission at Day 50. The endpoint population was the full analysis set: participants who received at least one dose of study treatment and had at least one postdose efficacy measurement for response. The reported endpoint groups contain 11 participants for Treatment A and 14 for Treatment B. The record does not describe the handling of participants without a postdose response measurement beyond the stated population definition.

The registry record lists seven secondary outcomes, including DNA methylation, leukemia-free survival, overall survival, minimal residual disease at baseline and Day 50, time to complete remission, and times to neutrophil and platelet recovery. Numerical findings for these outcomes are not reported in the registry record. The record also does not report pharmacokinetic results despite identifying pharmacokinetics as a study objective. The available results therefore support a focused description of the primary response measure and the recorded safety counts, rather than a complete assessment of all study objectives.

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: A total of 98 participants were screened, of which 25 were enrolled and treated in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set included all participants who received at least one dose of study treatment and who had at least one postdose efficacy measurement for response.

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 included all participants who received at least one dose of study treatment and who had at least one postdose efficacy measurement for response.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Morphologic Complete Remission (CR), measured over Day 50.

The primary endpoint was the percentage of participants with morphologic complete remission at Day 50. It represents the proportion of the defined response population who met the study's remission criteria at that assessment time. The endpoint used bone marrow evaluations, such as biopsies, aspirates, or both, performed by local pathology laboratories and assessed by study investigators.

For a participant to be designated as having complete remission, the record required a morphologic leukemia-free state, an absolute neutrophil count (ANC) greater than 1000 per microliter (/mcL), and a platelet count greater than 100,000/mcL. Thus, the outcome combines a marrow-based assessment with specified blood-count criteria. It is not simply a count of participants with any improvement in disease measurements.

A Day 50 remission percentage provides a defined, clinically interpretable snapshot of response after induction treatment. In general, a binary response endpoint can be summarized as the number meeting the criteria relative to the number assessed in each group. It does not describe how long remission lasts, whether leukemia later returns, or survival over time. Those questions relate to other outcomes, such as leukemia-free survival and overall survival, which are listed as secondary outcomes but whose numerical results are not reported in the registry record.

The posted percentages were 27.3% for Treatment A and 50.0% for Treatment B. The endpoint description and analysis-population definition matter when interpreting these values: the percentages refer to the stated response population and Day 50 assessment, not necessarily every person initially enrolled.

7. Results Posted in the Registry

• Treatment B: Induction Chemotherapy Only: 50.0% (7/14) versus 27.3% (3/11) on control; risk difference 22.7 percentage points (95% CI -14.4 to 59.9), risk ratio 1.83 (0.61–5.50); unadjusted two-proportion z-test p = 0.250.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either met the stated complete-remission criteria by Day 50 or did not. A percentage summarizes the share meeting those criteria within an analysis group. For Treatment A, the reported percentage was 27.3% among 11 participants; for Treatment B, it was 50.0% among 14 participants. Because each participant contributes a discrete outcome, a small number of responses can noticeably affect the percentage. This is one reason to consider interval estimates alongside point estimates.

What does a confidence interval express?

In general, a confidence interval describes uncertainty around an estimate under the assumptions of the method used. It is not a range of individual participant outcomes, and it does not assign a probability to a fixed treatment effect after the data have been observed. The registry reports a 95% confidence interval for each group percentage: 6.0 to 61.0 for Treatment A, and 23.0 to 77.0 for Treatment B. Their breadth indicates that the observed percentages do not pin down the underlying response proportions precisely.

A comparative analysis can express the difference between groups in absolute terms or use a relative measure. The recalculated unadjusted risk difference for Treatment B relative to Treatment A was 0.227, with a 95% confidence interval from -0.144 to 0.599. The interval includes zero, the value corresponding to no difference on the risk-difference scale. The recalculated unadjusted risk ratio was 1.833, with a 95% confidence interval from 0.612 to 5.497; the recalculated unadjusted odds ratio was 2.667, with a 95% confidence interval from 0.492 to 14.46. The relative intervals include the value corresponding to no relative association. These statements describe the interval locations, not proof of no effect.

Why consider more than one effect scale?

In general, the risk difference describes an absolute contrast in response probabilities, while the risk ratio compares those probabilities multiplicatively. The odds ratio compares odds rather than probabilities. These measures answer related but different questions, and their numerical magnitudes are not interchangeable. With sparse binary outcomes, relative estimates can be especially imprecise. Readers should identify the scale and its interval before interpreting a reported estimate.

The unadjusted p-value was 0.25. In general, a p-value quantifies how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it quantify clinical importance. A p-value should be interpreted together with the estimated effect, its confidence interval, the design, and the amount of information in the data.

What does randomization contribute?

In general, random assignment aims to make treatment groups comparable in expectation, reducing systematic differences at the start of a study. It does not guarantee balance in every realized sample, particularly when groups are small. The registry identifies the study as randomized but does not report the sequence-generation method, allocation concealment, stratification, or other implementation details. It also does not report whether the posted comparison was adjusted for any baseline factors. The comparison is therefore an unadjusted recalculation from the posted summary statistics.

The endpoint population was the full analysis set, defined as participants who received at least one dose and had at least one postdose efficacy measurement. In general, restricting an analysis to those with a measurement can affect interpretation if missingness is related to treatment or outcome. The record does not report the number or outcomes of participants excluded from this endpoint population, reasons for missing measurements, or sensitivity analyses addressing missing data.

The registry record contains no additional analysis records and does not report the study's original statistical plan. It is therefore not possible to determine from the record whether the endpoint comparison was prespecified in the posted form, whether any covariate adjustment was planned, or whether additional analyses were performed but not entered. General concepts about binary outcomes and uncertainty help explain the posted estimates, but they do not fill in those missing protocol details.

10. Confidence Intervals and Precision

The two group percentages have broad 95% confidence intervals. For Treatment A, the reported response percentage was 27.3%, with an interval from 6.0 to 61.0. For Treatment B, it was 50.0%, with an interval from 23.0 to 77.0. The intervals show that the underlying response percentages are not estimated narrowly from these groups. In general, a confidence interval is a way of expressing sampling uncertainty around an estimate; it does not guarantee that the true value lies inside the interval.

The unadjusted risk-difference estimate for Treatment B relative to Treatment A was 0.227, with a 95% confidence interval from -0.144 to 0.599. The interval spans values below and above zero, so the data do not locate the absolute difference precisely. The unadjusted risk ratio was 1.833, with an interval from 0.612 to 5.497, and the unadjusted odds ratio was 2.667, with an interval from 0.492 to 14.46. These relative-effect intervals are also broad and span values on either side of the no-association value.

The reported unadjusted p-value of 0.25 is consistent with substantial uncertainty in the comparison, but it should not replace the effect estimate and interval. In general, statistical precision is about how tightly the data constrain plausible values, whereas a p-value addresses compatibility with a particular null model. Neither measure alone conveys whether an effect would be important in practice.

The small endpoint groups are an important context for the width of these intervals. The percentages are useful descriptions of the observed participants, but they are not precise estimates of response in a larger population. The registry record does not report further interval methods or adjusted estimates. Interpretation should therefore remain tied to the posted unadjusted summaries and their uncertainty.

11. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. The original sample-size justification and statistical design assumptions are not reported in the registry record. For this binary endpoint, the planning figures are participants per arm, not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one. The 90% power column gives the corresponding number per arm for a 90% chance. These are design-planning quantities, not counts from the trial. For example, the listed requirements for planning at 75% of the observed effect are 123 participants per arm for 80% power and 165 participants per arm for 90% power. At 50% of the observed effect, the listed figures are 268 and 358 participants per arm, respectively.

Smaller effects generally require more participants to distinguish them from random variation under otherwise comparable assumptions. The table's larger planning figures for smaller fractions illustrate that principle. The illustration is anchored to an effect estimated from a small study, so it should not be mistaken for a stable forecast of the effect a future trial might observe. These figures are not observed power.

For time-to-event outcomes, a sample-size display may instead report a total number of events; that is not the format used for the binary remission endpoint. Any curve associated with the planning display should be read as a visual representation of the same assumptions, rather than as additional observed trial evidence.

12. 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 = 0.273; treatment proportion p₁ = 0.500; average p̄ = 0.386.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6886 = 1.3496.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6696 = 0.5635.
4. n = (1.3496 + 0.5635)² / (0.2273)² = 70.9, rounded up to 71 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 <- 0.272727272727273                          # control proportion
p1 <- 0.5                          # 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(1177540)
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 = 71 (80% power), 95 (90% power)
 75% of observed effect: n per arm = 123 (80% power), 165 (90% power)
 50% of observed effect: n per arm = 268 (80% power), 358 (90% power)
power.prop.test: 70.9 
Simulated power at n = 71 per arm: 0.800 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome: the percentage of participants with morphologic complete remission at Day 50. It also lists seven secondary outcomes, covering DNA methylation, leukemia-free survival, overall survival, minimal residual disease, time to complete remission, and recovery times for neutrophils and platelets. Numerical results for these secondary outcomes are not reported in the registry record. Their absence means that the posted primary result cannot be placed alongside a complete set of listed outcomes.

When a study examines multiple outcomes or multiple analyses, the chance of at least one apparently notable result can increase. In general, multiplicity methods may control or otherwise address that issue, but the registry record does not report a multiplicity strategy. It also does not report the original statistical analysis plan, any hierarchy among outcomes, or whether secondary results were adjusted for multiple testing. It is therefore not possible to assess how multiplicity was handled in the study.

The full analysis set included participants who received at least one dose of study treatment and had at least one postdose efficacy measurement. The registry record does not report how many enrolled participants lacked a qualifying postdose measurement, why any measurements were missing, or how missing endpoint data were handled. It also does not provide sensitivity analyses for missing data. In general, missing outcome measurements can affect a treatment comparison if the likelihood of missingness differs by treatment or is related to response.

The record identifies the study as randomized but does not provide a detailed analysis population flow or participant disposition for the primary endpoint. The difference between enrollment and the endpoint group counts cannot be explained from the registry record alone. No additional analysis records are listed, and details about exclusions, protocol deviations, or alternative analysis populations are not reported in the registry record. These limitations constrain evaluation of robustness and selective reporting.

14. 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: appendicitis (9.1%), large intestine perforation (9.1%), lower gastrointestinal hemorrhage (9.1%), sepsis (7.1%).

The posted safety counts list serious adverse events for 2 of 11 participants in Treatment A and 1 of 14 participants in Treatment B. Other adverse events were recorded for 8 of 11 participants in Treatment A and 9 of 14 in Treatment B. The record also lists 3 deaths in each group. These are counts associated with the treatment groups; the summary does not establish that an event was caused by a study treatment.

The serious-event terms listed include Appendicitis, Large intestine perforation, and Lower gastrointestinal hemorrhage, each at 9.1%, and Sepsis at 7.1%. The record does not map those listed terms to treatment arms in the available summary. The percentages and counts should be read as registry safety reporting, not as comparative risk estimates.

In general, adverse-event counts describe events recorded during a study and need context about definitions, observation time, severity, and attribution. The registry record does not provide detailed exposure duration, event timing, or causality assessments in this summary. The small groups also make these counts difficult to interpret as precise estimates of event frequency. They are descriptive safety information, not proof that a treatment caused or prevented an event.

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

The posted primary result describes the proportion of the endpoint population meeting the study's morphologic complete-remission criteria by Day 50. That percentage was 27.3% for Treatment A, decitabine plus induction chemotherapy, and 50.0% for Treatment B, induction chemotherapy only. The result is a comparison of observed responses in this study, not a definitive statement about the effect of either regimen in a wider population.

Uncertainty is substantial. The 95% confidence intervals for the group percentages are 6.0 to 61.0 for Treatment A and 23.0 to 77.0 for Treatment B. The unadjusted risk-difference interval runs from -0.144 to 0.599, while the unadjusted relative-effect intervals are also broad. The data therefore do not provide a precise estimate of the comparative response. The unadjusted p-value of 0.25 does not demonstrate that the treatments are equivalent, and it does not show that there is no effect.

The outcome applies to a defined assessment at Day 50. It does not establish the duration of remission, leukemia-free survival, overall survival, or changes in minimal residual disease. Although those outcomes appear among the listed secondary outcomes, their numerical findings are not reported in the registry record. The study summary also names safety and pharmacokinetics as objectives, but the available record does not provide pharmacokinetic results.

The reported safety counts are descriptive and should not be interpreted as proof of treatment causation. The registry status is terminated, but the reason is not reported in the registry record. Details of the original sample-size justification, analysis plan, missing-data procedures, and multiplicity approach are also not reported. The result is best understood as a limited, imprecise summary from a small randomized study, rather than as a standalone basis for a clinical decision.

16. Why This Trial Matters Statistically

This trial illustrates why a numerical difference between two observed percentages is not enough to characterize a randomized comparison. The Day 50 remission percentages were 27.3% in Treatment A and 50.0% in Treatment B, but the endpoint groups were small and the confidence intervals broad. The estimates communicate both the observed response and the substantial uncertainty around it.

The example also shows the importance of choosing and naming an effect scale. An absolute risk difference, a risk ratio, and an odds ratio describe the same binary endpoint in different ways. Here, the recalculated unadjusted estimates have wide confidence intervals, so none provides a narrow account of the comparative effect. Readers need the interval as well as the point estimate to judge how much information the data contain.

Registry interpretation also depends on transparent reporting beyond the primary endpoint. This record identifies a full analysis set and several secondary outcomes, but numerical secondary findings, missing-data details, multiplicity methods, and the original statistical plan are not reported in the registry record. Those gaps make it harder to assess whether the primary comparison represents the complete planned analysis and how robust it is to alternative assumptions.

Finally, the sample-size illustrations distinguish planning from evidence observed in the trial. They show how assumptions about the effect to detect and desired power relate to participant requirements, but they are not the original design justification and are not observed power. Together, these features make the study a useful example of reading an estimate, its precision, and its reporting context as a connected whole.

17. 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 endpoint groups are small: 11 participants in Treatment A and 14 in Treatment B. The confidence intervals around the remission percentages are broad, and the unadjusted comparative intervals also span a wide range. The resulting estimates are therefore imprecise. The registry record does not report whether the group sizes reflect the originally planned allocation or a change during the study.

The record reports a terminated status but does not give the reason for termination. It does not report the planned enrollment, the original sample-size justification, or the statistical assumptions used to design the study. The planning illustration associated with the observed effect should not be mistaken for the trial's original design rationale.

The study is described as randomized and open label, but details about sequence generation, allocation concealment, stratification, and treatment implementation are not reported in the registry record. The endpoint was assessed by study investigators using local pathology evaluations, and masking was absent. The record does not describe procedures for central review or other safeguards against assessment bias.

The full analysis set requires at least one postdose efficacy measurement. The record does not explain how many enrolled participants did not meet that definition, why any measurements were unavailable, or how missing responses were treated. It also does not report sensitivity analyses, baseline-adjusted comparisons, or the full analysis plan. Numerical findings for listed secondary outcomes are not reported in the registry record, limiting interpretation of survival, minimal residual disease, recovery, and pharmacokinetic objectives.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Efficacy and Safety of Decitabine as Epigenetic Priming With Induction Chemotherapy in Pediatric Acute Myelogenous Leukemia (AML) Subjects — NCT01177540.
• Registry record last updated 2022-06-28; status last verified 2013-10.
• Results first posted 2022-06-28.
• 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.

21. Record Summary

NCT01177540 is a randomized, open-label, multicenter, parallel-group phase 2 study of decitabine as epigenetic priming with induction chemotherapy in pediatric acute myelogenous leukemia. The study compared decitabine plus induction chemotherapy with induction chemotherapy only. It enrolled 25 participants, began on 2011-03-03, had a primary completion date of 2013-07-19, and is listed as terminated.

The primary endpoint was the percentage with morphologic complete remission at Day 50 in the stated full analysis set. The reported values were 27.3% for Treatment A and 50.0% for Treatment B, with broad 95% confidence intervals. The unadjusted comparison is imprecise. The registry lists secondary outcomes and safety counts, but numerical secondary outcome results and several design and analysis details are not reported in the registry record.