Tamibarotene Plus Venetoclax/Azacitidine in Participants With Newly Diagnosed Acute Myeloid Leukemia (AML): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tamibarotene Plus Venetoclax/Azacitidine in Participants With Newly Diagnosed Acute Myeloid Leukemia (AML) (NCT04905407), a randomized phase 2 study. The primary outcome is Part 2: Complete Remission/Complete Remission With Incomplete Hematologic Recovery (CR/CRi) Rate.

2. Clinical Question

The question concerns a response outcome: whether participants achieved one of two defined remission states during follow-up of up to 3 years. It is not a direct comparison of survival, time to relapse, or quality of life. The registry record identifies the response assessment as investigator-determined.

The trial was designed around a specific biological population: adults with previously untreated AML selected for RARA-positive disease and unable to receive standard induction therapy. The Part 2 comparison therefore addresses the added tamibarotene regimen in that selected setting. It does not directly answer whether the same comparison applies to people with AML who do not meet those eligibility characteristics.

The registry record reports randomized Part 2 groups and response estimates, but the small analyzed groups and broad confidence intervals matter when interpreting the comparison. The observed percentages are estimates from the participants who entered the primary analysis population, not guarantees of what would occur in another group. The registry record does not report the reason the trial was terminated.

3. Trial Design

This was a phase 2, randomized, open-label, parallel-group trial sponsored by Syros Pharmaceuticals. The registry records enrollment of 66 participants and lists acute myeloid leukemia as the condition. The trial began on 2021-08-26, had a primary completion date of 2024-08-12, and is listed as terminated. The reason for termination is not reported in the registry record.

The study included more than one part. Part 1 evaluated the three-drug combination, and the Part 2 regimen was selected from Part 1. Part 2 randomized participants to tamibarotene with venetoclax and azacitidine or to venetoclax and azacitidine alone. In the primary efficacy analysis, the mITT population included RARA-positive participants randomized in Part 2 who started dosing from Cycle 1 Day 1. The group sizes in that analysis were 25 and 26.

Part 3 allowed some Part 2 participants receiving venetoclax and azacitidine to begin subsequent treatment with tamibarotene added after progressive disease, relapse after an initial CR or CRi response, or treatment failure. Part 3 is therefore not another randomized comparison of the initial Part 2 strategies. Its participants and treatment history differ from those in the primary comparison.

Open-label means treatment assignment was not masked. The registry record does not report masking of outcome assessment or further details about randomization procedures, such as how the allocation sequence was generated. The record lists 14 outcome measures and no separately reported analysis entries. Specific details of the statistical analysis plan, including any interim analyses, 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: As per sponsor decision, the study was terminated.

Part 1 and Part 2

Reasons for not completing this period:

Part 3

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Part 1 Safety Analysis Set included all enrolled participants who received any amount of study treatment (tamibarotene, venetoclax, or azacitidine).

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: Part 1 and Part 3 safety population included all enrolled participants who had received any amount of study drug (tamibarotene, venetoclax, or azacitidine). Part 2 intent to treat (ITT) population included all participants who were randomized in Part 2. Treatment groups for this population were determined according to the treatment assignment at the time of randomization. Data of Part 3 participants is being reported separately.

6. Primary Endpoint

The registry lists the primary outcome as Part 2: Complete Remission/Complete Remission With Incomplete Hematologic Recovery (CR/CRi) Rate, measured over Up to 3 years.

The primary endpoint was the Part 2 CR/CRi rate: the percentage of participants who achieved complete remission (CR) and/or complete remission with incomplete hematologic recovery (CRi), as determined by the investigator, over a timeframe of up to 3 years. The analysis population was the Part 2 mITT set: RARA-positive participants who were randomized and started dosing from Cycle 1 Day 1.

CR required an absolute neutrophil count of at least 1,000/µL, a platelet count of at least 100,000/µL, bone marrow blasts below 5%, and no circulating blasts, blasts with Auer rods, or extramedullary disease. CRi used the same marrow and disease criteria, but allowed either neutrophils or platelets not to have recovered: the absolute neutrophil count was below 1,000/µL and the platelet count was below 100,000/µL, with all CR criteria met except for recovery of either neutrophils or platelets.

Combining CR and CRi recognizes remission when marrow and disease criteria are met even though blood-count recovery is incomplete. This can provide a broader response measure than CR alone. As a general statistical point, a binary response endpoint is easy to express as a proportion, but it does not convey how long a response lasted or what happened after the assessment. Those are distinct questions; the registry lists duration outcomes separately.

7. Results Posted in the Registry

• Part 2: Venetoclax/Azacitidine: 69.2% (18/26) versus 60.0% (15/25) on control; risk difference 9.2 percentage points (95% CI -16.9 to 35.4), risk ratio 1.15 (0.77–1.74); unadjusted two-proportion z-test p = 0.490.

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.

Part 2: Complete Remission (CR) Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Venetoclax/Azacitidine: 57.7% (15/26) versus 48.0% (12/25) on control; risk difference 9.7 percentage points (95% CI -17.6 to 37.0), risk ratio 1.20 (0.71–2.03); unadjusted two-proportion z-test p = 0.488.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Venetoclax/Azacitidine and the control. The interval gives the range of effects that remain compatible with the data.

Part 2: Complete Remission/ Complete Remission With Partial Hematologic Recovery (CR/CRh) Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Venetoclax/Azacitidine: 57.7% (15/26) versus 48.0% (12/25) on control; risk difference 9.7 percentage points (95% CI -17.6 to 37.0), risk ratio 1.20 (0.71–2.03); unadjusted two-proportion z-test p = 0.488.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Venetoclax/Azacitidine and the control. The interval gives the range of effects that remain compatible with the data.

Part 2: Overall Response Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Venetoclax/Azacitidine: 73.1% (19/26) versus 80.0% (20/25) on control; risk difference -6.9 percentage points (95% CI -30.1 to 16.2), risk ratio 0.91 (0.67–1.24); unadjusted two-proportion z-test p = 0.560.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Venetoclax/Azacitidine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary response outcomes provide related but distinct views of remission and overall response. Taken together, the posted percentages do not form a uniform pattern in which one initial regimen is consistently higher across every response measure. Their confidence intervals are broad, and the comparisons are not reported with adjusted analyses. These features call for a cautious, descriptive reading rather than treating any one secondary endpoint as confirmation of the primary comparison.

CR alone is narrower than the primary CR/CRi endpoint because it does not include remission with incomplete hematologic recovery. CR/CRh uses a different definition of incomplete recovery, while overall response captures a broader response category. These outcomes can help describe the types of response observed, but their definitions are not interchangeable. A difference in one measure does not necessarily imply a similar difference in another.

These secondary results should be considered alongside, not instead of, the primary CR/CRi result. They can add context about response categories, but they do not establish that a treatment strategy has a broader effect on survival, duration of benefit, or other outcomes. The registry lists duration outcomes and adverse events among its outcomes, but separate inferential analyses for the secondary response comparisons are not reported.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for an apparently notable finding to arise by chance. Unless an analysis plan identifies which outcomes are confirmatory and how multiplicity will be addressed, individual secondary comparisons are better treated as descriptive or hypothesis-generating. The registry record does not report a multiplicity strategy for these endpoints. This limitation is additional to the sampling uncertainty reflected in the confidence intervals.

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

• Part 1: Overall Response Rate (ORR)
• Part 1: Plasma Concentration of Tamibarotene
• Part 2: Number of Participants With Treatment Emergent Adverse Events
• Part 2: Complete Remission (CR) Rate
• Part 2: Complete Remission/ Complete Remission With Partial Hematologic Recovery (CR/CRh) Rate
• Part 2: Duration of Complete Remission
• Part 2: Duration of CR/CRi
• Part 2: Duration of CR/CRh

9. Statistical Interpretation

10. Statistical Methods Explained

The central statistical task is to estimate and compare two response proportions. The endpoint classifies each participant as having achieved CR or CRi, or not having achieved either response, and expresses the number with a response as a percentage of the analysis group. This makes the endpoint binary at the participant level, even though the clinical criteria used to define response involve several measurements.

What does randomization contribute?

Randomization assigns participants to treatment groups by chance. As a general statistical principle, this can make groups more comparable at the start of a study, including with respect to factors that were not measured. It supports an estimate of the contrast between the assigned treatment strategies. Randomization does not eliminate uncertainty, and in relatively small groups chance imbalances can remain. The registry record identifies the trial as randomized but does not report the allocation procedure or any stratification factors.

The parallel design means the Part 2 groups were assigned different initial regimens rather than all participants receiving both regimens in sequence. The comparison is between tamibarotene plus venetoclax and azacitidine and venetoclax plus azacitidine. Part 3 has a different role: it describes later addition of tamibarotene for some participants initially assigned to venetoclax and azacitidine after specified disease or treatment events. It should not be combined with the Part 2 randomized comparison as if it were a third randomized arm.

What does the confidence interval represent?

A confidence interval describes the statistical uncertainty around an estimated quantity. As a general explanation, a 95% confidence interval is produced by a procedure intended to cover the underlying quantity in 95% of repeated samples under the procedure's assumptions. It is not a statement that there is a 95% probability that the fixed, true value lies within this particular interval. For a response proportion, the interval communicates uncertainty in the estimated rate; for a difference, it communicates uncertainty in the contrast between groups.

The registry reports a 95% confidence interval for each arm's CR/CRi percentage and for the risk difference. The exact interval-construction procedure is not reported in the registry record. The interval for the difference is especially useful for understanding the comparison: values on either side of zero correspond to differences in opposite directions, and an interval that includes zero does not rule out no difference under the interval's method.

How should the p-value be read?

The registry lists an unadjusted p-value of 0.49 for the primary comparison. As a general explanation, a p-value measures how incompatible the observed data are with a specified null hypothesis under the test's assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A larger p-value does not prove that the groups are the same. The registry record does not report the test used or a prespecified threshold for interpreting this result.

“Unadjusted” indicates that this value is not presented as corrected for multiple comparisons. That matters because the registry includes several outcomes. Looking across multiple outcomes can increase the chance of seeing an apparently notable result by chance. Interpretation should consider the primary endpoint separately from exploratory or secondary findings, while recognizing that an adjustment strategy is not reported in the registry record.

Why can over-dispersion matter in general?

For binary outcomes, a simple statistical model may assume that outcomes vary according to a particular probability structure. As a general statistical point, over-dispersion means the observed variation is greater than that assumed by the model. If it is ignored, uncertainty estimates can be too narrow and tests can appear more conclusive than warranted. The registry record does not report an over-dispersion assessment or indicate that a model requiring such an assessment was used. This is a general consideration, not a claim that over-dispersion occurred in this trial.

The analysis population also defines what the percentages describe. Here, the primary population consisted of RARA-positive Part 2 participants randomized and starting dosing from Cycle 1 Day 1. It is narrower than a simple reference to everyone enrolled in the overall trial. The record does not explain how participants with missing response assessments were handled, whether all eligible participants had an endpoint assessment, or whether any additional sensitivity analyses were performed. Those details affect how fully the posted percentages can be interpreted.

Finally, an outcome defined by investigator assessment may involve judgment in applying clinical criteria. The open-label design means treatment assignment was not masked. General statistical reasoning suggests that knowledge of assignment can matter for some assessments, but the registry record does not say whether independent review was used. It would therefore be inappropriate to assume either that assessment was blinded or that assessment bias occurred.

11. Confidence Intervals and Precision

Precision is the degree to which an estimate is concentrated around a value. The primary arm-specific confidence intervals extend from 38.7% to 78.9% for the three-drug group and from 48.2% to 85.7% for venetoclax and azacitidine alone. The widths indicate substantial uncertainty around each estimated response percentage. The analysis groups contain 25 and 26 participants, so each participant's outcome has a meaningful influence on the group proportion.

The risk-difference interval, -0.169 to 0.354, spans zero and includes differences in either direction. It is therefore consistent with a range of possible comparative effects, rather than a narrowly estimated advantage for one group. The point estimate of 0.092 is only one location within that broad interval. Precision should be assessed from the full interval, not from the point estimate or p-value alone.

As a general statistical explanation, confidence intervals tend to be narrower when more information is available and wider when estimates are based on limited data or variable outcomes. A confidence interval does not address every source of uncertainty: it does not by itself account for possible bias, missing outcomes, limitations in endpoint assessment, or whether the study population represents a broader clinical population. The registry record does not report the method used to calculate these intervals, so their construction cannot be independently assessed from the record alone.

The secondary response intervals are also broad. Across endpoints, a close-looking pair of percentages should not be taken as evidence of close underlying rates when uncertainty remains substantial. Conversely, an interval that includes a null difference does not show that the true difference is exactly zero. The data are compatible with multiple possibilities, and the estimates should be read with that imprecision in mind.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are expressed as participants per arm for these binary response outcomes, not as a total number of events. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the assumed effect under the planning assumptions, if that effect and the other assumptions hold. The 90% power column describes the corresponding planning target with a 90% chance. These are design calculations, not probabilities that the trial's result is correct and not measures of how much information the completed trial actually had.

The rows consider planning for the full observed effect and for smaller fractions of that effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller. The observed effect used as the starting point is itself uncertain, especially with the small Part 2 groups and broad confidence intervals; the illustrations should not be treated as a reliable forecast of a future study's outcome.

These figures are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the completed results: the confidence intervals show the uncertainty in the estimates directly. The numbers also do not establish what the original trial was designed to detect, because that original design rationale is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.600; treatment proportion p₁ = 0.692; average p̄ = 0.646.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6762 = 1.3254.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6731 = 0.5665.
4. n = (1.3254 + 0.5665)² / (0.0923)² = 420.0, rounded up to 421 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 <- 0.6                          # control proportion
p1 <- 0.692307692307692                          # 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(4905407)
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 = 421 (80% power), 562 (90% power)
 75% of observed effect: n per arm = 759 (80% power), 1,015 (90% power)
 50% of observed effect: n per arm = 1,730 (80% power), 2,315 (90% power)
power.prop.test: 420 
Simulated power at n = 421 per arm: 0.794 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures, including remission, response, duration, plasma concentration, and treatment-emergent adverse events. Testing or interpreting many outcomes can increase the chance that at least one result appears noteworthy even when there is no corresponding underlying effect. A multiplicity strategy can define which outcomes are primary, how comparisons are ordered, and whether significance thresholds are adjusted. Such a strategy is not reported in the registry record.

The primary CR/CRi result should consequently be distinguished from secondary comparisons. The primary endpoint is identified in the record, but the record does not report a complete statistical analysis plan specifying hypotheses, analysis methods, handling of multiple comparisons, or any planned hierarchy. The listed unadjusted p-value should not be interpreted as if it were adjusted for the full set of outcomes.

Missing-data handling is also not reported in the registry record. In a response analysis, missing assessments can affect the denominator and can change the interpretation of a percentage, depending on the analysis rule. The primary population definition identifies participants who were randomized and started dosing from Cycle 1 Day 1, but it does not by itself explain the handling of participants without an evaluable response, withdrawals, or other incomplete follow-up. The record does not report sensitivity analyses addressing these possibilities.

The analysis population is described as mITT, not as all participants enrolled across every part of the trial. The primary analysis is restricted to eligible Part 2 participants who started dosing. The registry record does not report a separate intention-to-treat analysis or explain whether results differed under another analysis population. The treatment group safety denominators also differ from the primary efficacy group sizes, so those safety summaries should not be assumed to use the efficacy population.

Interim analyses, stopping boundaries, and any adjustments associated with interim monitoring are not reported in the registry record. The record identifies the trial as terminated but does not state why it ended or whether termination followed a planned decision rule. No conclusion about the reason for termination or its statistical implications can be drawn from the information reported.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (40.0%), neutropenia (30.0%), febrile bone marrow aplasia (20.0%), anaemia (20.0%), sepsis (20.0%).

Serious adverse event summaries use safety-group denominators that differ from the primary efficacy analysis groups. In Part 1, 10 of 10 participants were reported as experiencing a serious adverse event. In Part 2, the corresponding figures were 15 of 24 for the tamibarotene combination and 13 of 27 for venetoclax and azacitidine. In Part 3, 4 of 5 participants were reported with a serious adverse event. These are counts of participants affected, not counts of individual events.

The registry also reports deaths of 7, 7, 7, and 2 in the Part 1, Part 2 combination, Part 2 comparator, and Part 3 groups, respectively. The information does not establish that these deaths were caused by treatment. The listed serious terms include febrile neutropenia, neutropenia, febrile bone marrow aplasia, anaemia, sepsis, and pulmonary embolism; the reported percentages describe terms, not an overall comparative safety test.

Part 3 is a selected group receiving subsequent treatment, not a randomized safety comparison. Differences in group sizes, treatment history, and time at risk limit direct comparisons across parts. The registry record does not report adjusted safety analyses or causal attribution for the deaths.

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

The posted results describe a randomized comparison of two Part 2 regimens in a selected group of adults with RARA-positive AML who were ineligible for standard induction therapy. The primary response percentages are estimates for the participants included in the mITT analysis. The confidence intervals and risk-difference interval show that the comparison remains imprecise; the data do not establish a clear difference between the initial regimens on CR/CRi.

This does not mean the regimens are equivalent. A finding that does not rule out zero difference is not proof of identical effects, particularly when the interval also includes differences in either direction. Equivalence or non-inferiority would require a design and interpretation framework that the registry record does not report.

The response endpoint also has limits. It combines CR and CRi, is investigator-determined, and is measured over a timeframe of up to 3 years. It does not by itself describe survival, duration of remission, or the balance of benefits and harms. Those are separate questions, and the posted primary result should not be treated as an answer to them.

The evidence applies to the study's specific eligibility criteria, treatment regimens, and analysis population. It does not directly answer questions about other AML populations, other treatment strategies, or the later treatment course in Part 3. The safety summaries are descriptive and should not be interpreted as proof that an adverse event or death was caused by a study drug. No medical decision follows from these statistics alone.

17. Why This Trial Matters Statistically

This trial is statistically informative because it randomized a biologically selected AML population between a three-drug regimen and a two-drug comparator. Randomization makes a direct comparison possible, while the primary endpoint focuses on a defined remission outcome. The registry also reports group-specific estimates and confidence intervals, allowing readers to assess uncertainty rather than relying only on a single point estimate.

The small Part 2 analysis groups make precision central to interpretation. The intervals around the response percentages and their difference are broad. That means the observed point estimates cannot be treated as definitive evidence about the size or direction of a population-level difference. The unadjusted p-value does not resolve that uncertainty or establish equivalence.

The design also illustrates why endpoint definitions and analysis populations matter. CR/CRi combines two response states, and the primary population excludes participants who did not start dosing after randomization. Part 3 includes selected participants who received subsequent treatment, so its outcomes cannot be read as another randomized contrast. Keeping these distinctions clear prevents unlike groups and outcomes from being collapsed into one conclusion.

Finally, the record leaves important statistical details unreported, including missing-data methods, the analysis procedures, multiplicity handling, and the rationale for the sample size. These gaps do not erase the posted estimates, but they limit how fully readers can assess their robustness. The main statistical lesson is to consider the estimates, their uncertainty, population, and reporting gaps together.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The Part 2 efficacy groups are small, and the primary confidence intervals are wide. The resulting uncertainty limits how precisely the response rates and their contrast can be estimated. A randomized design helps with comparative interpretation, but it does not remove the uncertainty associated with limited group sizes.

The primary outcome is investigator-determined in an open-label trial. The registry record does not report whether response assessments underwent independent or blinded review. That leaves uncertainty about the assessment process; it does not establish that assessments were biased. The record also does not report the exact statistical methods used to produce the confidence intervals or the comparison p-value.

The primary analysis population includes participants who were randomized and started dosing from Cycle 1 Day 1. The registry record does not report how missing or unevaluable response assessments were handled, or whether an alternative analysis population was used. This makes it difficult to assess the potential influence of incomplete data or exclusions after randomization.

The registry does not report the original sample-size justification, a detailed analysis plan, multiplicity handling, interim analyses, or the reason for termination. Multiple secondary outcomes are listed, but separate inferential analyses are not reported for those outcomes. The safety summaries include different denominators across study parts and are not adjusted comparative analyses. Part 3 is a selected subsequent-treatment group and cannot be interpreted as a randomized arm.

Finally, the study population is restricted to previously untreated adults selected for RARA-positive AML who were ineligible for standard induction therapy. Results therefore have limited direct reach beyond that population. These are limitations of what the registry record can establish, not evidence that a particular unreported procedure or event occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Tamibarotene Plus Venetoclax/Azacitidine in Participants With Newly Diagnosed Acute Myeloid Leukemia (AML) — NCT04905407.
• Registry record last updated 2025-02-24; status last verified 2025-01.
• Results first posted 2025-02-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a randomized, open-label, parallel phase 2 trial of tamibarotene with venetoclax and azacitidine in adults with previously untreated, RARA-positive AML who were ineligible for standard induction therapy. Part 2 compared the three-drug combination with venetoclax and azacitidine alone.

The primary endpoint was the investigator-determined CR/CRi rate over up to 3 years in the Part 2 mITT population. The posted response estimates were 60% and 69.23%, with a risk-difference estimate of 0.092 and a 95% confidence interval from -0.169 to 0.354. The interval includes zero and is broad, indicating substantial uncertainty in the comparison.

The record lists enrollment of 66, a primary completion date of 2024-08-12, and trial status as terminated. It does not report the reason for termination, the original sample-size justification, detailed missing-data methods, or a multiplicity strategy. Secondary and safety results require descriptive interpretation, particularly because study parts and analysis populations differ.