Liposomal Cytarabine-Daunorubicin CPX-351 in Treating Patients With Untreated Myelodysplastic Syndrome or Acute Myeloid Leukemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Liposomal Cytarabine-Daunorubicin CPX-351 in Treating Patients With Untreated Myelodysplastic Syndrome or Acute Myeloid Leukemia (NCT01804101), a randomized na study. The primary outcome is Treatment-related Mortality Rate. (TRM).

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group clinical trial with no masking reported. The registry records an enrollment of 48 participants. The lower-dose arm included 38 participants, while the higher-dose arm included 10. The higher-dose arm was closed to accrual effective 4/21/14, so the groups were not equal in size. The registry status is completed. The phase is recorded as not applicable.

The trial studied liposomal cytarabine-daunorubicin CPX-351 in patients with untreated myelodysplastic syndrome or acute myeloid leukemia. Its official title specifies adults with untreated high-risk MDS and non-APL AML at high risk of treatment-related mortality. The intervention record also lists laboratory biomarker analysis, but no biomarker results are included in the outcome information. The registry identifies Fred Hutchinson Cancer Center as sponsor.

The lower-dose treatment description specifies CPX-351 given intravenously over 90 minutes on days 1, 3, and 5, with treatment repeating every 40 days for up to 4 courses in the absence of disease progression or unacceptable toxicity. The higher-dose description gives the same schedule and notes its closure to accrual. Participants achieving CR or CRp were described as continuing to consolidation, but the remainder of that treatment description is truncated in the registry record. Further detail on the protocol, including any dose-specific modifications, is not reported in the registry record.

The primary outcome was treatment-related mortality, with assessment up to 1 month after completion of study treatment. Overall remission rate, combining CR and CRp, was posted as a secondary outcome with a timeframe up to day 28. The registry also reports counts for adverse events and deaths. The record does not report further details of randomization procedures, allocation concealment, trial blinding, or the original statistical 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.

Overall Study

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.

6. Primary Endpoint

The registry lists the primary outcome as Treatment-related Mortality Rate. (TRM), measured over Up to 1 month after completion of study treatment.

The primary endpoint is treatment-related mortality, recorded as a count of participants. The registry gives its assessment timeframe as up to 1 month after completion of study treatment. In the posted results, 6 participants in the lower-dose arm and 2 in the higher-dose arm had this outcome. These are event counts within groups of different sizes, so the counts alone do not describe the relative frequency without considering each arm’s enrollment.

Treatment-related mortality is included because the stated study question concerned patients considered at high risk of mortality related to treatment. The registry frames the objective as estimating whether either or both CPX-351 dose levels might improve the treatment-related mortality rate while keeping the CR rate constant. This wording states the aim; it does not establish that the trial met that aim or that the dose groups were equivalent on remission.

The endpoint is a binary participant-level outcome for the posted comparison: each participant either contributes to the count or does not. The record does not define the specific criteria for attributing a death to treatment, explain how competing causes were adjudicated, or specify how participants without complete endpoint information were handled. Those definitions and procedures are not reported in the registry record, so interpretation should remain tied to the recorded endpoint label and timeframe.

7. Results Posted in the Registry

• Arm II (Closed to Accrual Effective 4/21/14): 20.0% (2/10) versus 15.8% (6/38) on control; risk difference 4.2 percentage points (95% CI -23.2 to 31.6), risk ratio 1.27 (0.30–5.35); unadjusted two-proportion z-test p = 0.751.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Overall Remission Rate (CR+CRp)

• 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:
  • Arm II (Higher Dose COX-351): 10.0% (1/10) versus 26.3% (10/38) on control; risk difference -16.3 percentage points (95% CI -39.6 to 7.0), risk ratio 0.38 (0.05–2.63); unadjusted two-proportion z-test p = 0.275.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Higher Dose COX-351) and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: overall remission rate, defined as CR+CRp, with assessment up to day 28. The results describe 10 participants with remission in the lower-dose arm and 1 in the higher-dose arm. The unadjusted comparison has a p-value of 0.275, and its confidence interval spans values on both sides of no difference. Taken together, the posted secondary results do not precisely establish the direction or magnitude of a remission contrast.

This endpoint relates to the primary question because the registry frames the study objective as estimating treatment-related mortality while keeping the CR rate constant. However, the posted remission comparison is not a test of equivalence, and no equivalence margin is reported. A result that does not show a clear difference cannot be taken to show that remission rates were the same. The secondary endpoint therefore gives contextual information about remission in the observed groups but does not resolve the stated objective’s condition about keeping CR constant.

Secondary results generally carry less weight than a prespecified primary analysis when the number of outcomes or comparisons is larger, because repeated testing can increase the chance of apparently noteworthy findings. The registry does not report a multiplicity strategy, a testing hierarchy, or an adjustment for multiple comparisons. Only one secondary endpoint is posted in the record, but the absence of a reported plan still limits how confirmatory its result can be considered. The registry lists no reported analyses, and the original analysis plan is not reported in the registry record.

The secondary outcome should consequently be read alongside, not as a replacement for, the primary endpoint. It does not establish that one dose maintained remission while changing treatment-related mortality, nor does it demonstrate that any observed pattern is a reliable dose effect. Its estimates are based on the same limited, unequal groups and are subject to similar uncertainty. The most defensible summary is that the registry reports remission counts and an unadjusted comparison, while leaving the interpretation of that contrast uncertain.

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

• Overall Remission Rate (CR+CRp)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are binary participant counts. For each arm, a participant either had the stated endpoint or did not. The primary comparison is described with an unadjusted risk difference, alongside relative risk and odds ratio summaries, confidence intervals, and an unadjusted p-value. These measures answer related but distinct questions. The risk difference expresses an absolute contrast between the arm-specific event proportions; the relative risk compares those proportions as a ratio; and the odds ratio compares event odds. The registry does not report an adjusted model for these comparisons.

What does a risk difference represent?

A risk difference is the event proportion in one group minus the event proportion in the reference group, using the direction indicated by the comparison. A value on the positive side indicates a higher observed event proportion in the comparison group; a value on the negative side indicates a lower one. A value near zero indicates little estimated absolute contrast. The estimate is only one part of the result: its uncertainty interval and the group sizes affect how strongly it can be interpreted. For the primary outcome, the posted interval spans both sides of zero.

How should the relative measures be read?

A relative risk compares event proportions, while an odds ratio compares event odds. For either measure, a value at the null reference corresponds to no relative contrast. Relative measures can sound more dramatic or more modest than an absolute difference depending on the baseline frequency. They also become unstable when event counts are sparse. The primary comparison includes only 8 endpoint events across both arms, so the relative estimates should be interpreted with their wide uncertainty intervals rather than as precise descriptions of a stable effect. The posted results do not report an adjusted analysis or a model incorporating additional participant characteristics.

What does the confidence interval add?

A confidence interval communicates uncertainty around an estimated effect under the method used to construct it. In general, a wider interval indicates less precision: many effect values remain compatible with the observed data and the calculation’s assumptions. An interval crossing the no-difference value does not prove that there is no effect. It means the data do not pin down the direction and size of the contrast with sufficient precision to exclude that value under the interval procedure. The primary interval extends across values on both sides of no difference, underscoring the limited precision of this comparison.

What does the p-value say?

The unadjusted p-value is a measure of how unusual data at least as inconsistent with a no-difference model would be if that model and the calculation’s assumptions held. It is not the probability that the null hypothesis is true, and it is not the probability that the result occurred “by chance.” The primary p-value is 0.751. That result is not evidence that the groups are equivalent, and it does not quantify the probability that one dose is better. The registry does not report the test procedure used for the original trial analysis, so no specific test should be inferred from the posted p-value alone.

Why do small event counts matter?

When event counts are limited, a small change in the number of participants with an event can noticeably change an estimated proportion or relative measure. Small groups also provide less information for estimating uncertainty. Here, the higher-dose arm contains 10 participants, and the primary endpoint count in that arm is 2. This makes the arm’s estimate particularly sensitive to the experience of a small number of participants. Unequal allocation does not invalidate a comparison by itself, but it means that the smaller arm contributes less information and can widen uncertainty.

For binary outcomes, the displayed summaries do not involve a dispersion parameter in the way that a count model or continuous-outcome model might. General statistical context: over-dispersion matters when observed variability exceeds what a chosen model assumes, because standard errors and intervals may otherwise be too small. The registry does not report a model for over-dispersion, and the primary endpoint is posted as a participant count rather than a modeled rate. There is therefore no basis for claiming that an over-dispersion adjustment was used or needed in the trial’s own analysis.

The comparisons shown are unadjusted calculations from the posted summary statistics. They do not account for covariates, stratification, or other design features unless those are explicitly part of the calculation, and the registry does not report such adjustments. The discrepancy indicator is false, so the posted summaries do not flag a disagreement with a sponsor analysis. Even so, the registry lists no reported analyses, and the trial’s original statistical methods are not reported in the registry record. The calculated comparisons should not be mistaken for a complete protocol-defined analysis.

General explanation: randomization is intended to make treatment groups comparable on average, but it cannot guarantee balance in every realized trial, especially when groups are small. The registry states that the trial was randomized, but does not report the randomization method, allocation concealment procedures, or stratification factors. No assumptions about those procedures should be added to interpretation of the posted estimates.

11. Confidence Intervals and Precision

Precision concerns how narrowly the observed data constrain an estimated effect. The primary risk-difference interval is broad and includes values on both sides of no difference. This means the registry’s estimate does not identify a precise direction or size of the difference in treatment-related mortality between the two dose groups. The interval is not a range of outcomes that contains a fixed proportion of individual participants; it describes uncertainty about the estimated contrast under the interval method.

The arm sizes help explain that uncertainty. The lower-dose group contains 38 participants and the higher-dose group contains 10. The smaller group contributes limited information, and the primary outcome is based on 6 events in one arm and 2 in the other. With limited event information, estimates can shift substantially with a small number of outcomes, and the resulting interval can remain wide. The registry’s unadjusted p-value of 0.751 is consistent with the fact that the posted data do not sharply distinguish the groups, but it is not itself a measure of precision.

The secondary remission comparison is also uncertain. Its posted interval includes values on both sides of no difference, and its unadjusted p-value is 0.275. That result should not be read as proof of no remission difference or proof that remission was held constant. The record does not report a clinically important threshold for either endpoint, so it is not possible to assess whether the intervals rule out differences that would matter to the study’s objective.

Confidence intervals depend on the statistical method and assumptions used to construct them. The registry does not describe the interval procedure or provide the original analysis plan. Accordingly, the intervals are useful for conveying uncertainty in the posted comparisons, but they do not fill gaps in the record about endpoint definitions, missing observations, adjustment, or the trial’s prespecified analysis.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s own design calculations. For these binary outcomes, the figures are participants per arm. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

Each row represents a planning scenario that uses a different share of the observed effect: 100%, 75%, or 50%. Within a scenario, the 80% power column gives the participants per arm indicated by the calculation for an 80% chance of detecting that assumed effect under the planning assumptions, if the effect and assumptions hold. The 90% power column gives the participants per arm for a higher target chance of detection under the same assumptions. These are design-planning quantities, not guarantees for a future study.

The sample-size curve should be read as a visual expression of the same relationship between assumed effect size and the number of participants needed. Smaller effects are harder to distinguish from random variation and therefore require more participants. The figures are not a reconstruction of the trial’s enrollment target, and they do not show how likely the observed result was to be detected after the trial was completed. This is not observed power.

For the primary outcome, the planning values are large because they use the observed treatment-related mortality contrast as their reference effect. For the remission outcome, the corresponding planning illustrations use its own observed contrast. These quantities should not be compared as if they were clinical judgments about the importance of either endpoint. They are conditional on the chosen effect fraction and the listed statistical assumptions. In particular, equal allocation in the illustration differs from the observed arm sizes, and the illustration does not incorporate unreported design features or any original protocol-based assumptions.

13. How the Sample Size Is Derived

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

Formula

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 = 0.158; treatment proportion p₁ = 0.200; average p̄ = 0.179.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5421 = 1.0625.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5413 = 0.4555.
4. n = (1.0625 + 0.4555)² / (0.0421)² = 1,299.8, rounded up to 1,300 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 <- 0.157894736842105                          # control proportion
p1 <- 0.2                          # 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(1804101)
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 = 1,300 (80% power), 1,740 (90% power)
 75% of observed effect: n per arm = 2,258 (80% power), 3,023 (90% power)
 50% of observed effect: n per arm = 4,960 (80% power), 6,639 (90% power)
power.prop.test: 1299.8 
Simulated power at n = 1,300 per arm: 0.805 (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 one primary outcome and one secondary outcome in the results. It does not report how the outcomes were prioritized in the original analysis plan, whether there was a formal testing hierarchy, or whether the analysis accounted for multiple testing. Multiplicity matters when several outcomes or comparisons are examined: without a prespecified approach, the chance of an apparently unusual result can increase as more analyses are considered. No correction or adjustment should be assumed.

The registry reports 0 analyses and no reported analyses for the secondary outcome. This means the record does not describe a protocol-defined statistical analysis in enough detail to assess model choice, covariate adjustment, or planned handling of the endpoints. The posted arm comparisons are unadjusted summaries. The registry does not report interim analyses, stopping rules, or a statistical monitoring plan. Those procedures should not be inferred from the randomized design or from the fact that the higher-dose arm closed to accrual.

Missing-data handling is also not reported in the registry record. The posted group sizes are given, but the record does not explain whether every randomized participant was included in each endpoint analysis, how participants without endpoint assessments were treated, or whether any values were imputed. The data therefore do not support a claim that the outcomes were analyzed under an intention-to-treat, per-protocol, or other defined analysis population. The precise analysis population for each endpoint is not reported in the registry record.

The record does not provide a sample-size justification for the original trial, the assumptions used to set enrollment, or a prespecified target effect. The planning figures accompanying the posted outcomes are illustrations based on observed effects and stated calculation assumptions; they do not recover the original design rationale. The protocol’s definition of treatment-related mortality and its adjudication process are not reported either. These omissions leave important questions about endpoint assessment, analysis populations, and inferential procedures unanswered.

These reporting gaps do not erase the observed counts, but they constrain how far interpretation can go. The registry supports a description of the posted results and their unadjusted uncertainty. It does not support reconstruction of a full statistical analysis plan or confirmation that all analyses followed a prespecified approach.

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 non-serious adverse event terms

The adverse-event record lists serious adverse events affecting 0 of 38 participants in the lower-dose arm and 0 of 10 in the higher-dose arm. It also lists other adverse events affecting 38 of 38 participants in the lower-dose arm and 10 of 10 in the higher-dose arm. These are recorded participant counts; they do not describe the number of individual event episodes or their severity distribution. No serious adverse-event terms are listed.

The registry lists 10 deaths in the lower-dose arm and 5 in the higher-dose arm. These death counts are not the same measure as the primary treatment-related mortality endpoint. The adverse-event record does not specify that all deaths were treatment-related, and the endpoint attribution and timing should not be inferred from the death totals. The adverse-event record’s follow-up timeframe and collection details are not reported in the registry record.

Zero recorded serious adverse events should be interpreted as the posted count, not as proof that serious events were impossible or that all safety risks were absent. Group sizes differ, and the higher-dose arm is small. The registry’s adverse-event entries provide a limited account of recorded events, not a complete characterization of safety or a causal comparison between doses.

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

The results establish what was recorded in this trial: treatment-related mortality occurred in 6 participants in the lower-dose group and 2 participants in the higher-dose group, and the registry’s unadjusted comparison is imprecise. The confidence interval crosses the no-difference value, and the unadjusted p-value is 0.751. The record therefore does not provide a precise estimate that resolves the direction or size of the difference between dose groups.

The results do not establish that the doses are equivalent. A failure to show a clear difference is not the same as evidence that the outcomes are the same. The study objective’s reference to keeping CR rate constant also does not demonstrate that remission was maintained: the remission outcome is reported as a secondary result, without an equivalence margin or a reported equivalence analysis. The available record does not show that the stated objective was met.

The sample-size illustrations do not indicate the probability that this completed trial would detect an effect, and they are not a substitute for the original design justification. They describe planning needs under stated assumptions and effect scenarios. Likewise, the posted unadjusted p-values do not quantify clinical importance, the probability that a treatment effect exists, or the probability that the null hypothesis is true.

The trial was randomized, but the registry does not report details of randomization, allocation concealment, endpoint adjudication, missing-data procedures, analysis populations, or the original statistical plan. The comparison also involves unequal and limited arm sizes, with the higher-dose group closed to accrual. These features restrict precision and limit assessment of how closely the reported summaries follow a prespecified analysis.

The appropriate statistical conclusion is narrow: the registry reports observed endpoint counts and uncertain unadjusted comparisons in this trial. The data do not establish a definitive difference, equivalence, or a causal explanation for the recorded outcomes. They also do not determine how the findings apply outside the population and treatment setting described in the registry record. No treatment recommendation follows from these statistics.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of how randomization does not guarantee a precise comparison when the realized groups are small and unequal. The higher-dose arm has 10 participants, compared with 38 in the lower-dose arm, and the primary outcome occurs in a limited number of participants. The resulting uncertainty is important: the observed contrast alone cannot give a stable account of the dose-group difference.

It also illustrates why a nonsignificant result cannot be equated with equivalence. The study objective refers to reducing treatment-related mortality while keeping the CR rate constant, but the registry does not provide an equivalence margin or a reported analysis designed to establish that condition. The remission outcome is secondary and uncertain. Without a defined margin and an appropriate design, absence of a clear difference is not evidence that remission was held constant.

The planning illustrations offer another statistical lesson. Sample-size needs depend on the effect being targeted and on assumptions such as allocation and the significance level. Smaller assumed effects require more participants. Those calculations are separate from the original trial design and do not make the observed result more or less persuasive after the fact.

Finally, the registry record shows why completeness of statistical reporting matters. Without details on analysis populations, missing data, multiplicity, interim monitoring, and original design assumptions, readers cannot fully reconstruct the intended inferential framework. The posted estimates and intervals still describe the available results, but their scope should remain limited to what the record documents.

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.

The main trial-specific limitation is the small, unequal allocation: 38 participants are listed in the lower-dose arm and 10 in the higher-dose arm. The higher-dose arm was closed to accrual effective 4/21/14. The reason for closure and its implications for recruitment or analysis are not reported in the registry record. The imbalance reduces the information available from the smaller group and makes the comparison sensitive to a small number of outcomes.

The endpoint is labeled treatment-related mortality, but the record does not provide its detailed definition, attribution rules, or adjudication procedures. The timeframe is given as up to 1 month after completion of study treatment, but handling of incomplete follow-up is not described. It is also not reported how the endpoint counts relate to the separate death totals in the adverse-event record.

The registry does not report the trial’s original sample-size justification, a prespecified effect of interest, analysis populations, missing-data methods, interim analyses, multiplicity handling, or the full statistical analysis plan. There is no reported protocol-defined method that would establish whether remission was kept constant. The secondary comparison is not a substitute for such an analysis.

The arm descriptions and outcome labels are not fully uniform. The higher-dose arm is marked as closed to accrual, and the secondary outcome record uses a different spelling of the drug name in its arm label. The treatment description is also truncated after noting continuation to consolidation for participants achieving CR or CRp. These record-level limitations make it important to rely on the stated dose-group labels and posted endpoint information rather than infer additional protocol detail.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Liposomal Cytarabine-Daunorubicin CPX-351 in Treating Patients With Untreated Myelodysplastic Syndrome or Acute Myeloid Leukemia — NCT01804101.
• Registry record last updated 2018-05-25; status last verified 2018-04.
• Results first posted 2018-05-25.
• 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 record describes a completed randomized, parallel-group trial of CPX-351 in adults with untreated high-risk MDS or non-APL AML at high risk of treatment-related mortality. It records 48 participants: 38 in the lower-dose arm and 10 in the higher-dose arm, which closed to accrual effective 4/21/14. No masking is reported.

The primary endpoint was treatment-related mortality up to 1 month after completion of study treatment. The posted counts were 6 in the lower-dose arm and 2 in the higher-dose arm. The unadjusted comparison is imprecise and does not establish a clear difference. The secondary endpoint was overall remission rate (CR+CRp) up to day 28; its comparison is also uncertain.

The registry does not report the original statistical plan, sample-size justification, analysis populations, missing-data procedures, multiplicity approach, or interim analyses. The posted results support description of the recorded outcomes, but not a definitive conclusion about dose equivalence or whether remission was maintained.