A Trial to Find and Investigate a Safe Dose of BI 836858 in Combination With Decitabine for Patients With Acute Myeloid Leukemia (AML): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial to Find and Investigate a Safe Dose of BI 836858 in Combination With Decitabine for Patients With Acute Myeloid Leukemia (AML) (NCT02632721), a randomized phase 1, phase 2 study. The primary outcome is Phase I: Number of Patients With Dose Limiting Toxicity (DLT(s)) During First Treatment Cycle.

2. Clinical Question

3. Trial Design

NCT02632721 is a completed Phase I/II trial sponsored by Boehringer Ingelheim. The registry lists randomized allocation, no masking, and a sequential model. Enrollment is listed as 49. The trial began on 2016-06-16, and primary completion is listed as 2023-01-16. These registry-level design labels do not, by themselves, describe how allocation operated within each phase or how participants were assigned to the reported dose groups.

The Phase I dose-escalation groups received BI 836858 at 20 mg, 40 mg, or 80 mg, each with intensive decitabine. The Phase I extensions evaluated 80 mg BI 836858 with either intensive or standard decitabine. The registry summary describes the Phase I objectives as determining the maximum tolerated dose and a recommended dose, then gathering additional safety, pharmacokinetic, and efficacy data to define a recommended Phase II dose.

The summary describes a Phase II objective of investigating efficacy, safety, and pharmacokinetics for the combination compared with decitabine monotherapy. The posted primary endpoint result instead concerns Phase I dose-limiting toxicity in the first treatment cycle. The reported groups and extension comparison are not a reported Phase II result comparing the combination with monotherapy. Details of the Phase II allocation, analyses, and outcome estimates are not reported in the registry record.

Phase I dose selection and a later comparative phase address different questions. Dose escalation focuses on toxicity and dose choice; a comparative efficacy question requires an interpretable contrast between treatment groups and an appropriate outcome analysis. The registered objectives therefore provide context, but should not be read as evidence that every objective has a posted result.

4. Participant Flow and Accounting

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

Before assignment: All subjects were screened for eligibility prior to participation in the trial. Subjects attended a specialist site which ensured that they (the subjects) strictly met all inclusion and none of the exclusion criteria. Subjects were not to be allocated to a treatment group if any of the entry criteria were violated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Treated set: All subjects who were documented to have received at least one dose of trial medication.

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: Treated set: The treated set includes all patients who have received at least one dose of study medication (BI 836858 and/or decitabine).

6. Primary Endpoint

The registry lists the primary outcome as Phase I: Number of Patients With Dose Limiting Toxicity (DLT(s)) During First Treatment Cycle, measured over Up to 28 days (first treatment cycle)..

The primary endpoint is the number of participants with one or more dose-limiting toxicities (DLTs) during the first treatment cycle, defined in the record as up to 28 days. It is a count of participants, rather than a measure of how many separate toxicity episodes occurred. The analysis population is the treated set: participants documented to have received at least one dose of trial medication.

The registry defines a DLT as a non-disease-related, non-haematological adverse event of Common Terminology Criteria for Adverse Events grade 3 or higher. It excludes expected non-haematological events related to the disease. The definition also identifies examples of complications arising from haematological events, including bleeding related to thrombocytopenia, infection related to neutropenia, and constitutional symptoms due to anaemia, as events not to be regarded as DLTs when defined by the Investigator.

In a dose-escalation setting, a first-cycle DLT count is used to describe whether a dose level produced toxicity meeting a prespecified threshold during the observation window. It can contribute to dose-selection decisions alongside other safety, pharmacokinetic, and efficacy information. It is not a complete summary of all safety experience: events outside the defined window or events that do not meet the DLT definition are not captured by this endpoint. The endpoint definition is reported, but further details of adjudication and handling of incomplete first-cycle observation are not reported in the registry record.

7. Results Posted in the Registry

• Phase I Extension A: BI 836858 80 mg + Decitabine (Intensive): 6.7% (1/15) versus 5.6% (1/18) on control; risk difference 1.1 percentage points (95% CI -15.4 to 17.6), risk ratio 1.20 (0.08–17.60); unadjusted two-proportion z-test p = 0.894.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a count endpoint represent?

The primary outcome counts participants who met the DLT definition during the first treatment cycle. Each participant contributes to the count according to whether at least one qualifying event occurred; multiple qualifying events in one participant do not turn the endpoint into a count of separate events. The groups report both the number with a DLT and the number in the treated set. The small denominators matter: a count of zero in a small group is not proof that the underlying risk is zero, and one event can substantially affect the observed group estimate.

Why are dose escalation and extension comparisons different?

Sequential dose escalation is designed to examine dose levels in an ordered process. Its purpose includes learning about toxicity as dose changes and informing dose selection. The posted arm descriptions show three dose levels with intensive decitabine, followed by two extensions at 80 mg using different decitabine schedules. The registry does not report the operational escalation rules or the full dose-selection algorithm, so those details cannot be inferred from the dose labels or counts.

The reported unadjusted comparison concerns the extension groups: 80 mg BI 836858 with intensive decitabine versus 80 mg with standard decitabine. It is a contrast between schedules in two Phase I extension groups, not an estimate of the Phase II comparison with decitabine monotherapy. A comparison is only interpretable for the particular groups, endpoint, and analysis stated; it does not automatically answer a broader objective in the trial summary.

How should the risk difference be read?

A risk difference expresses the difference between two event proportions. For this contrast, the reported estimate is 0.011. Its interval extends from -0.154 to 0.176, so values below and above zero are compatible with the reported interval. Zero corresponds to no difference on the risk-difference scale. The p-value of 0.894 is a measure of how unusual data at least as inconsistent with a zero-difference model would be under that model and the analysis assumptions; it is not the probability that the treatments are identical or that the null hypothesis is true.

A risk ratio compares event proportions by division, while an odds ratio compares event odds. The reported risk ratio is 1.2, with an interval from 0.082 to 17.6; the odds ratio is 1.214, with an interval from 0.070 to 21.22. For these relative measures, a value of one represents no relative difference. Their intervals are broad and include values on either side of one, reflecting substantial uncertainty. With sparse events, relative measures can be particularly unstable.

What does a confidence interval convey?

In general, a confidence interval describes the uncertainty associated with an estimate under a specified statistical procedure. It is not a range that guarantees the true value lies inside it, nor is it a direct probability statement about the parameter after the data have been observed. The confidence level for the posted extension intervals is not reported in the registry record. The interval widths are important alongside the point estimates: the risk-difference estimate is near zero, but the interval still permits appreciable differences in either direction.

What are the dose-rate probability summaries?

The registry gives probabilities for selected ranges of DLT rates for some dose-escalation groups. These are not the observed DLT counts and should not be read as event percentages. They are presented as probability summaries about a rate falling within specified intervals. The values and interval labels are reported, but the underlying model, prior assumptions, and decision rules are not reported in the registry record. The 40 mg entry with the truncated label does not allow its intended probability category to be identified confidently.

Why can over-dispersion matter in general?

In general, a basic binomial model assumes that participants within a group share a common event probability and that their outcomes are independent conditional on that probability. If outcomes vary more than that model allows, the data are over-dispersed relative to the model. Over-dispersion can make standard errors too small and intervals too narrow if it is ignored. This is a general statistical consideration, not a claim that over-dispersion was present or assessed in this trial. The registry record does not report enough detail to identify the model used for the dose-rate summaries or assess its fit.

The posted extension comparison is explicitly unadjusted. The record does not report a covariate-adjusted estimate for that contrast. The registered randomized allocation label does not supply missing details about assignment within the reported Phase I groups, nor does it establish which estimand or analysis population was used for every result. Interpretation should therefore remain tied to the posted group counts and the stated unadjusted comparison.

10. Confidence Intervals and Precision

The extension risk-difference estimate is 0.011, with an interval from -0.154 to 0.176. The estimate is close to zero, but the interval is wide relative to that estimate and includes both negative and positive values. On the reported scale, the data are compatible with an advantage in either direction as well as little difference. The confidence level for this interval is not reported in the registry record, so it should not be assigned a familiar level by assumption.

The relative-effect intervals are also broad. The risk ratio is 1.2, with an interval from 0.082 to 17.6; the odds ratio is 1.214, with an interval from 0.070 to 21.22. Both intervals include one, the no-relative-difference value. The low event counts and small extension groups limit precision, and the relative estimates are especially sensitive when events are sparse.

Precision concerns the range of values reasonably compatible with an estimate under the analysis procedure; it is distinct from whether a p-value crosses a threshold. A p-value of 0.894 does not make the estimate precise, and the interval does not demonstrate equivalence. No equivalence margin is reported in the registry record. The primary endpoint counts are also descriptive evidence from small groups: the observed zero counts during dose escalation do not rule out nonzero underlying DLT risk.

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 planning figures are participants per arm, not total events. They use the observed extension risk difference as a starting point and consider planning for 100% of that observed effect, 75% of it, and 50% of it. Under the stated assumptions, planning for 100% of the observed effect gives 7,295 participants per arm for 80% power and 9,765 participants per arm for 90% power. Planning for 75% gives 12,693 per arm for 80% power and 16,992 per arm for 90% power. Planning for 50% gives 27,937 per arm for 80% power and 37,400 per arm for 90% power.

The calculation assumes 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. The original trial’s own sample-size assumptions and justification are not reported in the registry record; these planning assumptions describe the illustration, not the trial’s original design.

In plain terms, the 80% power column gives the per-arm planning size associated with an 80% chance of detecting the specified effect under the calculation assumptions, if that effect and model assumptions hold. The 90% column expresses the corresponding planning size for a higher target chance of detection. Smaller effects require more participants, which is why the entries increase as the planned effect becomes a smaller fraction of the observed effect. These are planning illustrations, not observed power.

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 = 0.056; treatment proportion p₁ = 0.067; average p̄ = 0.061.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3388 = 0.6639.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3387 = 0.2850.
4. n = (0.6639 + 0.2850)² / (0.0111)² = 7,294.4, rounded up to 7,295 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 <- 0.0555555555555556                          # control proportion
p1 <- 0.0666666666666667                          # 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(2632721)
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 = 7,295 (80% power), 9,765 (90% power)
 75% of observed effect: n per arm = 12,693 (80% power), 16,992 (90% power)
 50% of observed effect: n per arm = 27,937 (80% power), 37,400 (90% power)
power.prop.test: 7294.4 
Simulated power at n = 7,295 per arm: 0.801 (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. Analyses Reported by the Sponsor

The registry reports dose-rate probability summaries for the Phase I escalation groups, including probabilities associated with selected DLT-rate ranges. These are different from the unadjusted extension comparison, which estimates a risk difference between the 80 mg intensive-decitabine and 80 mg standard-decitabine groups. The sponsor summaries address dose-level uncertainty; the recalculated extension contrast addresses a difference between two extension groups. They should not be treated as competing estimates of the same quantity.

The record does not flag a discrepancy between the posted result and the unadjusted recalculation. The reported dose-rate values include 0.081 for the 20 mg group in [0.16, 0.33), 0.028 for the 40 mg group in that range, and 0.012 for the 80 mg group in that range; the listed values for the [0.33, 1) range are 0 for the 20 mg and 80 mg groups. The 40 mg entry with a truncated label also has value 0, but its intended range is unclear. Further details of the sponsor’s model and assumptions are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The trial summary includes several objectives across Phase I dose escalation, Phase I extension, and Phase II, as well as safety, pharmacokinetic, and efficacy outcomes. The registry lists one secondary outcome: the number of Phase I participants with objective response (CR + CRi). The primary endpoint result is a Phase I DLT count, while the posted unadjusted comparison concerns the two extension schedules. These multiple questions and stages make it important to distinguish each reported analysis rather than treat them as one overall test.

Multiplicity refers, in general, to the increased chance of at least one false-positive result when many hypotheses are tested. A prespecified hierarchy, adjustment procedure, or other multiplicity strategy can help define how several tests should be interpreted. Such a strategy, including whether any adjustment was made for multiple outcomes or comparisons, is not reported in the registry record. The p-value of 0.894 is described as unadjusted; no adjusted p-value for the extension contrast is reported.

The primary endpoint specifies the treated set as participants documented to have received at least one dose of trial medication. The record does not report how missing first-cycle assessments, incomplete follow-up, treatment discontinuation, or other missing outcome data were handled. Imputation methods and sensitivity analyses for missing data are not reported. The analysis population used for every other outcome or for the extension comparison is also not reported in the registry record.

The registry record does not report a complete statistical analysis plan, interim-analysis procedures, or rules for stopping or selecting doses. It also does not report the original sample-size justification. These omissions limit assessment of whether all analyses followed prespecified procedures, how missing observations may affect estimates, and how the many objectives were prioritized. They do not change the posted counts, but they constrain the strength and scope of conclusions that can be drawn from them.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: malignant neoplasm progression (75.0%), febrile neutropenia (66.7%), device related infection (66.7%), diarrhoea (33.3%), non-cardiac chest pain (33.3%).

The serious adverse event summary reports, by group, the number at risk and the number affected. In the 20 mg intensive group, 4 participants were at risk and 4 were affected; in the 40 mg group, the corresponding figures are 3 and 3. For the 80 mg dose-escalation group, they are 9 and 8. In Phase I Extension A, they are 15 and 14; in Extension B, they are 18 and 17. The other-adverse-event counts list all participants at risk and affected in each of these groups.

The registry also lists deaths by group: 3, 2, 5, 11, and 13, respectively, across the five groups in the order. These are counts, not estimates of treatment-attributable mortality. The registry does not establish from these figures whether an event or death was caused by a study drug, the disease, or another factor. Exposure duration and further context for interpreting these counts are not reported in the registry record.

Among the listed serious adverse event terms, malignant neoplasm progression is shown as 75.0%; febrile neutropenia and device related infection are each 66.7%; diarrhoea, non-cardiac chest pain, and infection are each 33.3%. The denominator and grouping used for these term percentages are not reported in the registry record. These summaries describe reported safety events and should not be read as causal comparisons between schedules.

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

The primary results describe first-cycle DLT counts in five Phase I groups. No DLTs were recorded in the 20 mg, 40 mg, or 80 mg dose-escalation groups; one was recorded in each extension group. The endpoint uses a specific definition and a first-cycle observation window, so these counts do not represent every adverse event or all safety experience over the full trial.

The extension comparison estimates a small risk difference, but its interval includes zero and extends in both directions. The relative-effect intervals are also wide. Consequently, these results do not establish that the two extension schedules have the same DLT risk, nor do they establish a reliable difference. The result is not a Phase II comparison of BI 836858 plus decitabine with decitabine alone.

The DLT counts are relevant to the Phase I dose-finding objective, but they do not on their own establish a maximum tolerated dose or recommended Phase II dose. Those decisions may involve protocol rules and other information, including safety beyond the primary endpoint and pharmacokinetic or efficacy findings. The registry summary describes those objectives, while the details needed to assess the complete decision process are not reported in the registry record.

Likewise, the listed adverse events and deaths are descriptive group summaries. They do not establish that the combination caused or prevented an event, and the available figures do not support a comparative safety conclusion for the full trial. No comparative Phase II efficacy estimate is reported in the primary result. Statistical interpretation should therefore stay with the endpoint, groups, and estimates that the registry actually reports.

17. Why This Trial Matters Statistically

This trial illustrates why Phase I dose-finding results and Phase II comparative results should be kept conceptually separate. The registry describes both stages and several objectives, but the primary result available is a first-cycle DLT count from Phase I. A trial’s broad objective does not mean that every objective has a corresponding posted estimate, and a dose-escalation count is not a substitute for a later comparative efficacy analysis.

It also shows the importance of uncertainty when event counts are sparse. The extension groups each have one DLT, yet the estimated risk difference has a broad interval and the relative-effect intervals span a wide range. Point estimates alone can make a result look more definite than the evidence allows. The interval communicates how little precision these group sizes provide for the between-schedule contrast.

Finally, the record distinguishes observed outcomes from model-based dose-rate summaries and from planning illustrations. Observed counts, probability summaries, and hypothetical sample-size calculations answer different questions. Clear interpretation depends on keeping those quantities separate, recognizing the analysis population and endpoint window, and noting where model details, missing-data methods, and the original design rationale are not reported.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information reported for this trial. The primary endpoint is limited to DLTs during the first treatment cycle, defined as up to 28 days. It does not capture all adverse events over the full treatment period, and the registry does not report how participants with incomplete first-cycle observation were handled. The treated-set definition is available for the primary endpoint, but analysis-population details for the extension comparison and other outcomes are not reported.

The number of participants in each reported group is small, and the observed DLT counts are sparse. This limits the precision of both the group summaries and the extension contrast. The record reports an unadjusted comparison and does not report covariate adjustment, multiplicity handling, or a confidence level for the interval. The available extension comparison also contrasts intensive and standard decitabine schedules at 80 mg BI 836858; it is not the Phase II comparison with decitabine monotherapy described in the objectives.

The registry gives selected dose-rate probability summaries but does not report the underlying model, prior assumptions, or decision rules. One 40 mg entry has a truncated label. Details of the Phase I dose-escalation algorithm, Phase II analyses, missing-data methods, interim analyses, and original sample-size justification are not reported in the registry record. The safety summaries list events and deaths, but the available figures do not establish causality or provide the exposure context needed for a fuller comparison.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Trial to Find and Investigate a Safe Dose of BI 836858 in Combination With Decitabine for Patients With Acute Myeloid Leukemia (AML) — NCT02632721.
• Registry record last updated 2024-03-19; status last verified 2024-02.
• Results first posted 2024-03-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02632721 is a completed Phase I/II trial of BI 836858 with decitabine in patients with acute myeloid leukemia. The registry lists 49 enrolled participants and reports a Phase I primary endpoint counting participants with DLTs during the first treatment cycle. The posted counts are zero in each of the three dose-escalation groups and one in each of the two extension groups.

The unadjusted extension comparison reports a risk difference of 0.011, with an interval from -0.154 to 0.176 and p = 0.894. The interval and relative-effect estimates indicate substantial uncertainty. The registry describes a Phase II objective comparing the combination with decitabine monotherapy, but that comparative Phase II result is not reported in the primary result summarized by the available endpoint data.