SGI-110 in Adults With Untreated Acute Myeloid Leukemia (AML), Not Considered Candidates for Intensive Remission Induction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SGI-110 in Adults With Untreated Acute Myeloid Leukemia (AML), Not Considered Candidates for Intensive Remission Induction (NCT02348489), a randomized phase 3 study. The primary outcome is Number of Participants With a Complete Response (CR).

2. Clinical Question

3. Trial Design

This was a phase 3, multicenter, open-label, randomized, parallel-group study comparing SGI-110 (guadecitabine) with Treatment Choice. The registry lists an enrollment of 815 and marks the study completed. The recorded start date is 2015-03-19, and the primary completion date is 2018-05-31. The registry lists 408 participants in the SGI-110 group and 407 in the Treatment Choice group for the primary outcome.

The population was adults with previously untreated acute myeloid leukemia who were not considered candidates for intensive remission induction chemotherapy. The comparison is therefore specific to this clinical context; the record does not establish applicability to other AML populations or treatment settings.

SGI-110 was guadecitabine given subcutaneously at 60 mg/m^2 daily for 5 days (Days 1-5) in 28-day cycles. Treatment Choice allowed cytarabine, decitabine, or azacitidine. The record specifies cytarabine as 20 mg subcutaneously twice daily on Days 1-10 every 28 days, and decitabine as 20 mg/m^2 by a 1-hour intravenous infusion daily on Days 1-5 every 28 days. The azacitidine description states 75 mg/m^2 intravenously or subcutaneously daily on Days 1-7, but the remainder of its schedule is not reported in the registry record.

There was no masking of the study treatment assignment. For the primary response outcome, however, the best response was assessed using International Working Group 2003 AML response criteria by a blinded independent pathologist. That distinction matters: open-label treatment can affect experiences and care, while blinded assessment can limit knowledge of assignment influencing the response classification. The registry record does not report the detailed randomization procedure or the original design assumptions.

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: For the efficacy analysis (all randomized participants), the total duration was 38 months, with a median follow-up of 766 days (25.5 months), lower quartile follow-up of 671 days (22.4 months), and upper quartile follow-up of 896 days (29.9 months). For safety analysis (all treated participants), total duration was 51 months. Combining participants into a single group as part of the Treatment Choice arm was pre-specified as part of the study design.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The efficacy analysis set includes all randomized participants.

5. Baseline Characteristics

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

Population: All randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With a Complete Response (CR), measured over Up to 38 months (median follow-up of 25.5 months).

The primary endpoint is the number of participants whose best response was complete response (CR). It is a binary outcome at the participant level: each person is classified according to whether a CR was recorded as their best response. The registry defines the assessment using International Working Group 2003 acute myeloid leukemia response criteria and states that a blinded independent pathologist assessed response.

CR is used as a measure of disease response in this trial. It is distinct from outcomes such as survival, time spent outside the hospital, transfusions, or health-related quality of life. A response count alone does not describe how long a response lasted or whether other aspects of participants’ health changed. The registry lists duration of CR and several other outcomes separately, reflecting that these questions are not answered by the primary response count.

The recorded timeframe is up to 38 months, with median follow-up of 25.5 months. The efficacy analysis set includes all randomized participants. The primary outcome therefore summarizes response classification in that stated population; it should not be interpreted as a direct measure of every dimension of clinical benefit or harm.

7. Results Posted in the Registry

• Treatment Choice: 17.4% (71/407) versus 19.4% (79/408) on control; risk difference -1.9 percentage points (95% CI -7.2 to 3.4), risk ratio 0.90 (0.67–1.20); unadjusted two-proportion z-test p = 0.480.

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.

Number of Participants With Composite CR (CRc)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Treatment Choice: 22.4% (91/407) versus 22.8% (93/408) on control; risk difference -0.4 percentage points (95% CI -6.2 to 5.3), risk ratio 0.98 (0.76–1.26); unadjusted two-proportion z-test p = 0.882.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment Choice and the control. The interval gives the range of effects that remain compatible with the data.

Number of Days Alive and Out of the Hospital

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Treatment Choice: mean 105.70 versus 98.10 on control; difference 7.60 (95% CI -1.13 to 16.33), standardized effect d = 0.12; z-test p = 0.088.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment Choice and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the questions beyond best response. The registry lists composite CR, days alive and out of the hospital, progression-free survival, red blood cell or platelet transfusions, health-related quality of life measured with EQ-5D-5L and EQ-VAS, and duration of CR. These outcomes cover response, time, resource use, patient-reported health, and durability, and their results cannot be collapsed into a single summary without a prespecified framework.

The posted summaries for composite CR and days alive and out of the hospital show estimates with uncertainty, rather than a uniformly decisive pattern across outcomes. They do not overturn or independently settle the primary comparison. Each endpoint addresses a different question, and results from secondary measures should be interpreted alongside their definitions, follow-up, and analysis methods.

Unadjusted secondary results carry less weight as evidence for a definitive treatment difference when many outcomes are examined. Repeated testing increases the chance of apparently notable findings arising from random variation. The registry record does not report a multiplicity adjustment or a hierarchy specifying how secondary outcomes were to be tested. A secondary result can still be informative, but its evidential strength depends on the prespecified plan, completeness of reporting, and consistency with other relevant outcomes.

Several outcomes named in the registry are not accompanied by numerical results in the posted summaries described for this analysis. Their estimates and uncertainty are not reported in the registry record. Absence of a posted estimate should not be interpreted as evidence of no difference.

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

• Number of Participants With Composite CR (CRc)
• Number of Days Alive and Out of the Hospital
• Progression-free Survival (PFS)
• Number of Red Blood Cell or Platelet Transfusions
• Change in Health-related Quality of Life (QOL) Scores From Baseline: EQ-5D-5L
• Change in Health-related Quality of Life (QOL) Scores From Baseline: EQ-VAS
• Duration of CR

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count of participants with a best response of CR. For analysis, such a count is commonly expressed as a response rate: the number meeting the response definition relative to the number assessed in the group. Comparing rates puts the groups on a common scale even when their group sizes are not exactly the same. The registry also reports the counts and group sizes, so the observed response proportions can be understood in their participant context.

What does a risk difference express?

A risk difference subtracts one group’s event rate from the other group’s event rate. It is an absolute measure, expressed in the same units as the rates. A value of zero represents no observed difference on that scale; a positive or negative value indicates direction according to the specified subtraction order. The unadjusted recalculation gives a risk difference of -0.019 for Treatment Choice relative to SGI-110. The registry analysis reports the difference in the other direction, as 1.92 percentage points. Direction conventions matter when comparing results: changing the subtraction order changes the sign, not the underlying comparison.

How does the reported analysis differ from the recalculation?

The registry reports a Cochran-Mantel-Haenszel analysis of the difference in response rate. This is a method for comparing categorical outcomes while accounting for stratification. The registry record does not report the stratification details needed to explain precisely how that adjustment was implemented. The recalculated estimate is a simple unadjusted comparison from the posted group counts. It does not reproduce any adjustment or other analysis details that may underlie the registry result. The record marks no discrepancy between the reported and recalculated results, and the point estimates are consistent when expressed in the same direction.

For the primary outcome, the registry reports a 96% confidence interval and p = 0.482. The simple recalculation reports a 95% confidence interval and p = 0.48. These are not identical analysis outputs: they differ in method and reported interval level. The sponsor’s analysis should be read as the study’s reported analysis, while the unadjusted calculation provides a transparent comparison based on the posted summaries.

What does a p-value tell the reader?

In general, a p-value describes how unusual the observed data, or data more extreme, would be under a specified no-difference model and its assumptions. It is not the probability that the no-difference model is true, nor the probability that the observed result arose “by chance.” A p-value also does not measure the size or clinical importance of an effect. The point estimate and confidence interval are needed to understand the direction and precision of the comparison. The registry record does not report a prespecified primary significance threshold or a detailed testing hierarchy.

What does the confidence interval contribute?

In general, a confidence interval gives a range of values compatible with the data and the method used, while reflecting sampling uncertainty. A wider interval indicates less precision than a narrower interval. For the primary response-rate difference, the reported interval crosses zero, so it includes both a possible advantage in either direction. This is not proof that the groups are equivalent. A conclusion of equivalence requires a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

What should be kept in mind for other outcome types?

The registry also lists a continuous secondary outcome, days alive and out of the hospital, reported as a mean with a standard deviation. A mean difference compares group averages; its interpretation depends on the outcome scale and on how well the mean summarizes the distribution. Standard deviation describes spread among observations, whereas a confidence interval for a mean difference describes uncertainty about the comparison. They are not interchangeable. The registry’s posted secondary summaries also include response, survival, transfusion, quality-of-life, and duration outcomes. Each has its own definition and analysis requirements; the registry record does not report a complete statistical analysis plan for them.

Where recalculated values are shown, they are unadjusted calculations from the posted summary statistics. They are useful for understanding the arithmetic of a comparison, but they do not replace analyses that account for study design or participant-level information. Details such as missing-data handling, model covariates, stratification factors, and any interim analyses are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the observed data. The primary reported difference in response rate is 1.92 percentage points, and its 96% confidence interval ranges from -3.67 to 7.5. Because the interval crosses zero, the data are compatible with a difference favoring either group as well as with little difference. Its width also indicates that the observed point estimate should not be treated as an exact value for the underlying treatment contrast.

The unadjusted recalculation reports a risk difference of -0.019 for Treatment Choice relative to SGI-110, with a 95% confidence interval from -0.072 to 0.034. This interval likewise crosses zero. The two intervals use different analysis approaches and different reported confidence levels, so they should not be treated as interchangeable. Their direction and general message are consistent when the comparison order is aligned.

A confidence interval is not a guarantee that the true effect lies within its particular limits. In general, it describes the range generated by a method with stated long-run coverage properties, under its assumptions. The interval’s inclusion of zero does not prove no difference; its limits represent uncertainty about both direction and magnitude. Nor does the interval establish clinical importance, which requires context beyond statistical precision.

The reported p-value, p = 0.482, is consistent with substantial uncertainty about the primary comparison under the reported analysis. It should be read together with the estimate and interval rather than as a stand-alone verdict. The registry record does not report an equivalence margin or a noninferiority analysis, so the interval cannot be used to claim equivalence.

12. Planning a Similar Trial: Sample Size

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

The planning estimates are illustrations based on the observed effect, not a reconstruction of the trial’s original design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect, including 100%, 75%, and 50% of that effect. The original design assumptions and sample-size justification are not reported in the registry record.

For outcomes other than time-to-event outcomes, the planning figures represent participants per arm. For time-to-event outcomes, the figures represent the total number of events. Thus, the unit represented depends on the endpoint type; participants per arm should not be confused with total enrollment or total events.

The 80% power column gives the estimated number of participants per arm, or total events for a time-to-event endpoint, under the stated assumptions for a design with 80% power to detect the assumed effect. The 90% power column gives the corresponding estimate for a design with 90% power. In general, higher planned power requires more information, and smaller effects require more participants or events to detect reliably.

These are planning illustrations, not observed power. They depend on the effect chosen for planning and on the stated assumptions. Because the effect fractions are based on the observed effect, they should not be read as evidence that a future study will produce that effect or achieve the listed power.

13. How the Sample Size Is Derived

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

Formula

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 = 0.194; treatment proportion p₁ = 0.174; average p̄ = 0.184.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5480 = 1.0741.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5479 = 0.4611.
4. n = (1.0741 + 0.4611)² / (-0.0192)² = 6,406.5, rounded up to 6,407 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 <- 0.193627450980392                          # control proportion
p1 <- 0.174447174447174                          # 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(2348489)
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 = 6,407 (80% power), 8,577 (90% power)
 75% of observed effect: n per arm = 11,505 (80% power), 15,402 (90% power)
 50% of observed effect: n per arm = 26,144 (80% power), 34,998 (90% power)
power.prop.test: 6406.5 
Simulated power at n = 6,407 per arm: 0.797 (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. Analyses Reported by the Sponsor

The registry’s own reported primary analysis is a Cochran-Mantel-Haenszel comparison of response rates. It gives a difference of 1.92 percentage points, a 96% confidence interval from -3.67 to 7.5, and p = 0.482. This is the study’s reported result and should be distinguished from the unadjusted recalculation based directly on group counts.

The recalculation gives a risk difference of -0.019 for Treatment Choice relative to SGI-110, a 95% confidence interval from -0.072 to 0.034, and p = 0.48. Its comparison direction is reversed relative to the registry’s reported difference. Once the direction is aligned, the analyses are consistent in their general message: the point estimate is small and the interval includes no difference.

The recalculation is not an attempt to reproduce the Cochran-Mantel-Haenszel method. The registry record does not give the stratification details needed to recreate that analysis. The two reported interval levels also differ. Accordingly, the recalculation is best treated as a simple, unadjusted check on the posted counts, not as a replacement for the registry’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies the primary response outcome and lists secondary outcomes, but a detailed statistical analysis plan is not reported in the registry record. In particular, a prespecified hierarchy for testing primary and secondary outcomes, a multiplicity adjustment, and rules for interpreting multiple comparisons are not reported. When several outcomes are examined, the chance of finding at least one apparently notable result can rise unless the analysis accounts for repeated testing. This makes unadjusted secondary findings less conclusive than a result from a clearly prespecified testing strategy.

The primary efficacy population is described as all randomized participants. The registry does not provide enough detail to determine how missing primary response assessments were handled, whether all randomized participants had evaluable response data, or how deviations from the intended treatment were addressed. The method for handling missing data in the secondary outcomes is also not reported in the registry record. These details matter because exclusions or assumptions about missing observations can affect estimates and their uncertainty.

The record does not report interim analyses, stopping rules, or the original sample-size justification. It also does not specify the full set of adjustment factors used for the Cochran-Mantel-Haenszel analysis. These omissions limit independent assessment of the analysis plan and the relationship between the reported testing and the trial’s design.

Randomization supports a fair comparison in expectation, but it does not remove the need to understand analysis populations, outcome availability, and prespecified methods. Open-label assignment is another consideration for outcomes that may be influenced by care decisions or participant reporting; the primary response assessment was described as blinded, but the registry does not establish blinding for every secondary measure.

16. 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: pneumonia (29.2%), febrile neutropenia (25.2%), sepsis (15.5%), septic shock (4.3%), pyrexia (4.0%).

The registry reports serious adverse events for 401 participants at risk in the SGI-110 group, with 327 affected, and for 392 participants at risk in the Treatment Choice group, with 297 affected. For other adverse events, it reports 379 affected among 401 at risk in the SGI-110 group and 371 affected among 392 at risk in the Treatment Choice group. The registry also reports deaths of 341 and 344, respectively. These are descriptive counts; they do not by themselves establish that a treatment caused an event or death.

The listed serious adverse event terms include pneumonia (29.2%), febrile neutropenia (25.2%), sepsis (15.5%), septic shock (4.3%), pyrexia (4.0%), and acute kidney injury (3.8%). The registry record does not specify the group attribution or denominator for these listed term percentages in the registry record reported for this analysis, so they should not be assigned to a particular treatment group or interpreted as a comparative risk estimate.

Safety counts require context about event definitions, duration of exposure, follow-up, severity, and attribution. Those details are not fully reported in the registry record. The counts should therefore be read as descriptive safety information rather than as a complete comparative assessment.

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

The primary result describes the observed frequency of best response CR in the two randomized groups. The registry reports a small difference in response rates, with an interval that includes no difference and plausible values in either direction. This is evidence with uncertainty, not proof that the groups are identical and not a definitive demonstration that one group is superior.

The finding applies to the enrolled population described in the registry: adults with previously untreated AML who were not considered candidates for intensive remission induction chemotherapy. It should not be generalized automatically to people with different disease or treatment circumstances. The open-label design, the use of Treatment Choice regimens, and the recorded follow-up also shape how the result should be understood.

CR is one outcome among several. It does not, on its own, establish the duration of response, survival, time outside hospital, transfusion burden, quality of life, or overall safety. The registry lists these as separate outcomes, and the reported primary result cannot substitute for their analyses. Some secondary numerical results and detailed methods are not reported in the registry record.

Statistical uncertainty and clinical importance are related but distinct. The confidence interval describes uncertainty in the estimated response-rate difference; it does not determine what magnitude would matter clinically. The registry record does not report an equivalence or noninferiority margin, so the primary result cannot support a claim that the treatments are equivalent. Nor does a p-value establish that a difference is unimportant.

The most defensible reading is descriptive: the posted primary data show similar observed response counts relative to the group sizes, with uncertainty that does not rule out differences in either direction. Further interpretation depends on the broader efficacy and safety evidence, analysis details, and clinical context, rather than the primary endpoint alone.

18. Why This Trial Matters Statistically

This trial poses a statistical question in a population for whom intensive remission induction chemotherapy was not considered suitable: how to compare a randomized treatment assignment with a choice among several regimens. The result illustrates why a point estimate should be read together with its confidence interval. A small observed difference does not establish equivalence when the interval remains compatible with effects in either direction.

The design also highlights the distinction between open-label treatment and blinded outcome assessment. Knowledge of assignment can affect some aspects of care or reporting, while blinded independent pathology assessment can reduce the possibility that treatment knowledge influences the primary response classification. These design features are relevant to interpreting the particular endpoint, but they do not resolve every source of uncertainty.

Statistically, the comparison demonstrates the difference between a study-reported, stratification-based analysis and a simple unadjusted recalculation from group summaries. The estimates are directionally consistent after aligning their subtraction order, but their methods and interval levels are not identical. Understanding those distinctions helps prevent treating a recalculation as if it reproduced the full trial analysis.

Finally, the registry separates response from outcomes such as progression-free survival, time alive and out of hospital, transfusions, quality of life, and duration of CR. That separation is important: a single endpoint cannot represent every dimension of treatment effect. The record’s missing details on multiplicity, missing-data handling, and original design assumptions also show why transparent reporting is essential for a complete statistical interpretation.

19. Limitations

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

The registry record does not report the original sample-size justification, detailed statistical analysis plan, interim analyses, stopping rules, or prespecified testing hierarchy. Without these details, it is not possible to assess fully how the primary analysis, secondary testing, and trial size were planned. The original design assumptions should not be inferred from planning illustrations based on the observed effect.

The study was open-label, although the primary response assessment was performed by a blinded independent pathologist. The registry does not establish blinding for all other outcomes. Outcomes involving treatment decisions, hospital care, or participant-reported quality of life may be sensitive to knowledge of assignment, though the extent of any influence cannot be determined from the posted information.

Missing-data methods, reasons for missing assessments, and the handling of protocol deviations are not reported in the registry record. These details are important for evaluating whether the analysis population and observed outcomes faithfully represent randomized participants. The record describes the primary efficacy set as all randomized participants but does not provide the full analysis details needed to assess outcome completeness.

Treatment Choice consisted of multiple possible regimens, and the schedule for azacitidine is incomplete in the registry description. This limits the detail available for understanding the comparator as implemented. The numerical secondary results are also incomplete in the posted summaries, and methods for multiplicity are not reported. Finally, the response endpoint does not capture the full range of efficacy, durability, safety, or quality-of-life outcomes listed in the registry.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: SGI-110 in Adults With Untreated Acute Myeloid Leukemia (AML), Not Considered Candidates for Intensive Remission Induction — NCT02348489.
• Registry record last updated 2024-08-27; status last verified 2024-07.
• Results first posted 2021-01-14.
• 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.

23. Record Summary

NCT02348489 is a completed, randomized, phase 3, open-label, parallel-group study of SGI-110 (guadecitabine) versus Treatment Choice in adults with previously untreated AML who were not considered candidates for intensive remission induction chemotherapy. The registry lists enrollment of 815, a start date of 2015-03-19, and a primary completion date of 2018-05-31.

The primary endpoint was the number of participants with a best response of CR, assessed using International Working Group 2003 AML response criteria by a blinded independent pathologist. The registry reports 79 of 408 in the SGI-110 group and 71 of 407 in the Treatment Choice group. Its reported difference in response rate was 1.92 percentage points, with a 96% confidence interval from -3.67 to 7.5 and p = 0.482.

The reported interval includes no difference. The record also lists secondary efficacy, hospital, transfusion, quality-of-life, and safety outcomes, but important analysis details—including missing-data handling, multiplicity procedures, and the original sample-size justification—are not reported in the registry record.