Dociparstat Sodium (CX-01) Combined With Standard Induction Therapy for Newly Diagnosed Acute Myeloid Leukemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dociparstat Sodium (CX-01) Combined With Standard Induction Therapy for Newly Diagnosed Acute Myeloid Leukemia (NCT02873338), a randomized phase 2 study. The primary outcome is Number of Subjects Who Achieved Morphologic Complete Remission.

2. Clinical Question

3. Trial Design

This was an exploratory Phase II, randomized, open-label, multicenter, parallel-group study. Random allocation assigns participants to treatment groups by chance, which is intended to reduce systematic differences between groups at baseline. The registry record does not report the method used to generate or conceal the allocation sequence, or whether any stratification was used. The study had no masking, so participants and study personnel knew the assigned treatment. A parallel-group design means that assigned groups receive their respective regimens during the study rather than crossing over between regimens as part of the design.

The three groups were standard induction therapy with idarubicin and cytarabine, that same therapy with dociparstat 0.125 mg/kg/hr, and that same therapy with dociparstat 0.25 mg/kg/hr. The registry describes standard induction as the 7+3 regimen. The dociparstat groups received a 4 mg/kg initial bolus on Day 1, followed by continuous infusion during Days 1 to 7, in addition to induction therapy. The posted arm descriptions are truncated, so details beyond the visible regimens are not reported in the registry record.

The registry lists enrollment of 75 and marks the study completed. The reported primary outcome counts are based on 26 participants in the control group, 25 in the lower-dose group, and 24 in the higher-dose group. These group denominators describe the posted primary outcome data; the registry record does not explain whether all randomized participants were included or how any missing outcome data were handled. The original sample-size justification and the trial's own planned statistical analysis 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: Note that 2 randomized subjects did not receive study treatment: 1 subject in the control group and 1 subject in the dociparstat 0.25 mg/kg group. Therefore, these 2 subjects are not included in the safety analysis, but are included in the efficacy analyses.

Overall Study

Reasons for not completing this period:

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 Number of Subjects Who Achieved Morphologic Complete Remission, measured over During induction and re-induction phases of treatment (up to 60 days after the start of each treatment cycle).

The primary endpoint was the number of participants achieving morphologic complete remission during induction and re-induction, up to 60 days after the start of each treatment cycle. Complete remission was assessed using International Working Group criteria. The registry definition requires an absolute neutrophil count (ANC) >1000/microliter, platelet count >100,000, fewer than 5% blasts in bone marrow aspirate, no blasts with Auer rods, and no evidence of extramedullary disease. The outcome is therefore a binary classification at the participant level: the criteria are met or they are not recorded as met.

Complete remission is used in AML studies as a clinical response outcome because it combines blood-count recovery with findings in the bone marrow and the absence of certain disease manifestations. Requiring multiple criteria makes the endpoint more informative than a count of one laboratory measure alone. At the same time, a remission count does not by itself describe how long remission lasts, whether leukemia later returns, or survival. Those are separate outcomes, and the registry lists several such outcomes as secondary endpoints.

The posted counts were 14 of 26 participants in the control group, 8 of 25 in the 0.125 mg/kg group, and 11 of 24 in the 0.25 mg/kg group. The registry record does not report a detailed endpoint adjudication process or analysis population beyond the posted arm denominators.

7. Results Posted in the Registry

• Dociparstat 0.125 mg/kg: 32.0% (8/25) versus 53.8% (14/26) on control; risk difference -21.8 percentage points (95% CI -48.3 to 4.6), risk ratio 0.59 (0.30–1.17); unadjusted two-proportion z-test p = 0.115.
• Dociparstat 0.25 mg/kg: 45.8% (11/24) versus 53.8% (14/26) on control; risk difference -8.0 percentage points (95% CI -35.7 to 19.6), risk ratio 0.85 (0.49–1.49); unadjusted two-proportion z-test p = 0.571.

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 Subjects Who Achieved Composite Complete Remission

• 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:
  • Dociparstat 0.125 mg/kg: 36.0% (9/25) versus 61.5% (16/26) on control; risk difference -25.5 percentage points (95% CI -52.1 to 1.0), risk ratio 0.58 (0.32–1.07); unadjusted two-proportion z-test p = 0.068.
  • Dociparstat 0.25 mg/kg: 62.5% (15/24) versus 61.5% (16/26) on control; risk difference 1.0 percentage points (95% CI -26.0 to 27.9), risk ratio 1.02 (0.66–1.57); unadjusted two-proportion z-test p = 0.944.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.125 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.25 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Subjects Who Died by Day 30

• 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:
  • Dociparstat 0.125 mg/kg: 4.0% (1/25) versus 7.7% (2/26) on control; risk difference -3.7 percentage points (95% CI -16.5 to 9.1), risk ratio 0.52 (0.05–5.38); unadjusted two-proportion z-test p = 0.575.
  • Dociparstat 0.25 mg/kg: 12.5% (3/24) versus 7.7% (2/26) on control; risk difference 4.8 percentage points (95% CI -11.9 to 21.5), risk ratio 1.62 (0.30–8.90); unadjusted two-proportion z-test p = 0.571.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.125 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.25 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Subjects Who Died by Day 60.

• 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:
  • Dociparstat 0.125 mg/kg: 8.0% (2/25) versus 7.7% (2/26) on control; risk difference 0.3 percentage points (95% CI -14.5 to 15.1), risk ratio 1.04 (0.16–6.83); unadjusted two-proportion z-test p = 0.967.
  • Dociparstat 0.25 mg/kg: 12.5% (3/24) versus 7.7% (2/26) on control; risk difference 4.8 percentage points (95% CI -11.9 to 21.5), risk ratio 1.62 (0.30–8.90); unadjusted two-proportion z-test p = 0.571.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.125 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dociparstat 0.25 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span remission, survival, recovery, and early mortality. This breadth gives clinical context beyond the primary count of morphologic complete remission: composite complete remission is another response definition, while event-free and leukemia-free survival, overall survival, and remission duration address outcomes over time. Neutrophil and platelet recovery describe aspects of count recovery, and death by a specified day addresses early mortality. These endpoints answer related but distinct questions, so agreement or disagreement among them does not automatically confirm or overturn the primary result.

The overall pattern is not a consistent signal of improvement across all posted secondary outcomes. The groups do not show a uniform ordering across the posted counts, and the comparisons are uncertain. That broad pattern is compatible with the uncertainty in the primary remission comparisons rather than resolving it. The registry record does not provide reported formal analyses for the secondary outcomes, so they should not be treated as independent confirmatory tests or as evidence establishing a treatment effect.

Unadjusted secondary results carry less weight for several reasons. A study that examines many outcomes and multiple treatment comparisons creates more opportunities for chance findings. Without a prespecified hierarchy or multiplicity procedure, an isolated difference is difficult to distinguish from a result arising by chance. Further, time-to-event outcomes require information about event timing and censoring; a simple event count does not provide the same information as a survival analysis. The registry record does not report the analysis methods or risk sets for those outcomes.

Secondary endpoints can still be useful for generating hypotheses and identifying patterns that warrant careful study. Their interpretation is strongest when definitions, analysis populations, missing-data handling, and multiplicity plans are specified in advance. Those details are not reported in the registry record. They therefore offer descriptive context, but do not substitute for a well-specified primary analysis or a confirmatory study.

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

• Duration of Event-free Survival
• Time to Leukemia-free Survival
• Number of Subjects Who Achieved Overall Survival
• Number of Subjects Who Achieved Composite Complete Remission
• Duration of Morphologic Complete Remission
• Time to Recovery of Neutrophils
• Time to Platelet Recovery
• Number of Subjects Who Died by Day 30

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary event: whether a participant achieved morphologic complete remission under the registry's stated criteria. For a binary outcome, the risk in a group is the proportion of participants with the event among those included in that group's analysis. The risk difference compares two such proportions by subtracting the control-group risk from the intervention-group risk. A negative risk difference means the observed event proportion is lower in the intervention group; a positive value means it is higher. This is a general explanation of the measure, not a claim about causation.

What does the confidence interval describe?

A confidence interval expresses uncertainty around an estimated effect. In general, a narrower interval indicates greater precision, while a wider interval indicates that the data are compatible with a broader range of effects. If an interval for a risk difference includes zero, the data are compatible with no difference under the method used to construct that interval. It can also include meaningful differences in either direction, so inclusion of zero is not proof that the groups are equivalent. For both primary comparisons, the posted intervals include zero and extend across effects on either side of it.

The reported p-values are unadjusted. In general, a p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry record does not report the testing procedure used to obtain these p-values, nor does it report a prespecified significance threshold for the primary analysis. The sample-size planning illustration separately lists a two-sided significance level of 0.05; that planning assumption should not be mistaken for confirmation that the same threshold formed the trial's original analysis plan.

Why compare each dose with control?

The posted primary results make two comparisons: each dociparstat group against standard induction therapy alone. Each comparison has its own effect estimate, interval, and unadjusted p-value. A comparison against a shared control does not establish a difference between the two dose groups. A direct dose-to-dose contrast would require its own estimate and uncertainty assessment, which are not reported in the registry record. Multiple comparisons also make interpretation more cautious: considering several tests increases the chance that at least one result may appear notable by chance. The registry record does not report a multiplicity adjustment or a testing hierarchy.

Risk differences are expressed on an absolute scale and can be read as differences in event proportions. Relative risks and odds ratios are alternative ways to express binary comparisons, but the primary interpretation focuses on risk differences. A relative measure can sound large or small depending on the baseline event frequency; an absolute measure keeps the comparison tied to the difference in the observed proportions. Neither type of estimate removes uncertainty or confounding, and randomization does not prevent chance imbalance in a small study.

What are the limits of the posted analysis?

The record posts outcome counts and unadjusted comparison statistics, but lists no analyses under reported analyses. It does not describe a regression model, covariate adjustment, handling of protocol deviations, or the population used for analysis. It also does not report how missing outcome data were treated. These omissions mean the posted results cannot be assumed to reflect a particular standard analysis strategy. A randomized design supports causal interpretation when the analysis appropriately preserves the randomized groups and missingness is addressed, but the registry does not supply enough detail to verify those conditions for the reported results.

General statistical interpretation also depends on the endpoint definition and timing. The primary endpoint is assessed during induction and re-induction, up to 60 days after the start of each treatment cycle. A count of remission events over that period differs from a time-to-event analysis, which uses both whether an event occurred and when. The primary analysis does not estimate duration of remission or survival. Those questions are represented by separate secondary outcomes in the registry, with their own definitions and analysis requirements.

11. Confidence Intervals and Precision

The primary risk-difference intervals are wide and include zero in both comparisons. This means the posted data do not locate the difference precisely: values consistent with lower remission in a dociparstat group and values consistent with higher remission remain within the reported uncertainty range. The intervals should be read alongside the observed counts, not as a guarantee that the true effect lies within a narrow or clinically decisive band. The registry record does not report a prespecified threshold for what difference would be clinically important.

Uncertainty is expected in randomized studies with limited numbers of outcome observations. When only a modest number of participants contribute to each group, changing the outcome status of a few participants can materially affect the estimated proportions. The posted groups include 26 participants in control, 25 in the lower-dose group, and 24 in the higher-dose group. Those denominators help explain why the estimated effects remain uncertain; they do not justify treating the observed differences as stable estimates for a larger population.

A confidence interval crossing zero should not be interpreted as evidence that the treatments are identical. Establishing equivalence or noninferiority requires a prespecified margin and an analysis designed for that purpose; these are not reported in the registry record. Conversely, an observed difference does not establish a reliable treatment effect when the interval remains broad and the analysis is unadjusted. The intervals communicate the range of effects compatible with the data under the method used, while the trial's limited size and unreported analysis details constrain how much can be concluded.

The same caution applies to the secondary outcomes: their estimates also have uncertainty, and the record lists no reported formal analyses. Precision is not determined only by whether a p-value is below a threshold. It depends on the width of the interval and whether that interval meaningfully narrows the plausible effects. In this study, the primary comparisons leave substantial uncertainty about the direction and magnitude of any difference.

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 original trial design. For the binary outcomes in this record, 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 effect to detect is 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 describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column describes the corresponding number per arm for a 90% chance. Power is a design property for a particular assumed effect and analysis, not a guarantee that a study will produce a particular result. These figures are not observed power.

Rows based on 100%, 75%, and 50% of the observed effect illustrate how planning changes when the target effect is smaller than the effect seen in this study. Smaller effects require more participants to distinguish them from random variation under the same assumptions. The calculation is especially sensitive when the observed effect is small: planning to detect a fraction of a small observed difference can yield very large participant requirements. Such figures should not be treated as a recommendation, since the observed effect in a small exploratory study may be unstable and the original design assumptions are not reported.

The sample-size calculations compare two arms at a time and assume equal allocation between those two arms. They do not represent the total enrollment for a three-group trial, and they do not incorporate adjustments for multiple comparisons or missing outcomes. The figures are best read as conditional illustrations of the scale of a future study under stated assumptions, rather than as a retrospective judgment of whether the completed trial was adequately designed.

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 = 0.538; treatment proportion p₁ = 0.320; average p̄ = 0.429.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7000 = 1.3720.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6827 = 0.5746.
4. n = (1.3720 + 0.5746)² / (-0.2185)² = 79.4, rounded up to 80 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 <- 0.538461538461538                          # control proportion
p1 <- 0.32                          # 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(2873338)
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 = 80 (80% power), 106 (90% power)
 75% of observed effect: n per arm = 144 (80% power), 193 (90% power)
 50% of observed effect: n per arm = 328 (80% power), 438 (90% power)
power.prop.test: 79.4 
Simulated power at n = 80 per arm: 0.799 (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 a primary endpoint and multiple secondary outcomes, alongside two dociparstat-versus-control comparisons. Testing several outcomes and comparisons increases the chance of at least one apparently unusual result even if there is no true treatment effect. Statistical methods can address this through a prespecified hierarchy, family-wise error control, or other multiplicity procedures. The registry record does not report a multiplicity plan, a testing hierarchy, or adjusted p-values. The posted p-values are unadjusted and should be interpreted with that limitation in mind.

The registry record also does not report the analysis population used for the primary endpoint. It does not specify whether all randomized participants were analyzed according to their assigned groups, whether the analysis was restricted to participants receiving treatment, or whether another population was used. Such details matter because excluding participants after randomization can weaken the protection that randomization provides against systematic differences.

Missing outcome data are another unresolved issue. The record gives arm-specific denominators for the primary outcome but does not say whether these represent all randomized participants, whether any outcomes were missing, or how missingness was handled. It does not report imputation methods, sensitivity analyses, or reasons for unavailable outcomes. If the likelihood of a missing endpoint differs between groups or relates to the outcome, the observed counts may not represent the same underlying populations.

These absences do not establish that the trial had a particular flaw; they mean the relevant procedures are not reported in the registry record. They limit independent assessment of whether the posted comparisons follow a prespecified statistical plan and how robust they are to alternative assumptions. The exploratory Phase II label further supports cautious interpretation, while the record does not identify the trial's formal decision rules or confirmatory objectives.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (13.0%), disseminated intravascular coagulation (4.3%), arrhythmia (4.3%), colitis (4.3%), gastric ulcer (4.3%).

The registry reports serious adverse events among 7 of 25 participants in the control group, 8 of 25 in the 0.125 mg/kg group, and 13 of 23 in the 0.25 mg/kg group. For other adverse events, the reported affected counts are 25 of 25, 25 of 25, and 23 of 23, respectively. The record also lists deaths by group, but does not clarify their timing or relationship to treatment in this safety summary. These are descriptive counts and denominators; they do not establish whether a treatment caused an event or whether groups differ reliably in safety.

The most frequently listed serious adverse event term is febrile neutropenia, at 13.0%. Other listed terms are disseminated intravascular coagulation, arrhythmia, colitis, gastric ulcer, and ileus, each at 4.3%. The registry record does not make clear which arm-level population or event-counting rule underlies these term percentages. Serious adverse event categories may include events that differ in severity, timing, and clinical context; the aggregated numbers alone cannot characterize individual risk or comparative safety.

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

The posted results describe a randomized comparison of standard induction therapy alone with standard induction therapy plus either of two dociparstat doses in newly diagnosed AML. For the primary endpoint, the remission counts were lower in each dociparstat group than in the control group. The estimated risk differences were negative, but the intervals included zero and the unadjusted p-values do not provide conclusive evidence of a difference. The findings therefore indicate uncertainty, not proof that the regimens are equivalent and not proof that adding dociparstat causes worse outcomes.

The study's randomized design is valuable because it aims to make treatment groups comparable, but randomization does not eliminate chance variation, particularly in a relatively small exploratory study. The open-label design means treatment assignment was known, although the primary endpoint uses explicit remission criteria. The registry record does not describe outcome adjudication, analysis populations, missing-data methods, or the original statistical plan, so readers cannot assess those aspects fully.

The results also do not establish that one dociparstat dose is better than the other. Both posted comparisons are against the shared control group, and a direct dose-to-dose analysis is not reported. Nor do the primary counts answer questions about duration of remission, survival, or safety on their own. Those require examination of their separate outcome definitions and analyses, which are not comprehensively detailed in the record.

These data are most appropriately understood as exploratory comparative results. They can inform hypotheses and future research planning, but should not be taken as proof of efficacy, lack of efficacy, equivalence, or a causal safety difference. The sample-size illustrations are based on observed effects and are planning calculations, not evidence about the power actually achieved by the completed trial. Overall, the registry record leaves considerable uncertainty about the magnitude and direction of treatment effects.

17. Why This Trial Matters Statistically

This trial illustrates several statistical issues common in early randomized studies. A randomized parallel-group design supports a direct comparison, but the group sizes and number of events remain limited. As a result, the estimates can be imprecise even when outcome definitions are clinically structured. The primary intervals include no difference and also allow effects in either direction, showing why a point estimate alone is not enough for interpretation.

The study also demonstrates the difference between a primary endpoint and a collection of secondary measures. Remission counts, survival outcomes, recovery times, and early mortality each address different questions. When multiple outcomes and treatment comparisons are available, an isolated pattern can be misleading without prespecified priorities and appropriate control of multiplicity. The registry record does not report those procedures or formal analyses for the secondary outcomes.

Finally, planning based on an observed effect should be handled carefully. An exploratory estimate from a small trial may be unstable, and future sample-size requirements depend on assumptions about the effect a study aims to detect. The planning illustration makes this dependence visible, but it cannot reconstruct the rationale behind the original study design. A record can offer useful outcome counts and comparisons while still leaving important analysis details undocumented. Recognizing both the evidence and these limits is central to sound statistical interpretation.

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 registry record has important trial-specific reporting limitations. Although it identifies the study as randomized and open label, it does not report the randomization procedure, allocation concealment, stratification, or details of treatment adherence and protocol deviations. The posted arm descriptions are truncated, limiting interpretation of regimen details beyond those stated. The record also does not report the original sample-size justification or the planned statistical analysis.

For the primary endpoint, the record provides arm counts and unadjusted comparison statistics but does not describe the analysis population or how missing outcomes were managed. It does not report a formal sponsor analysis, covariate adjustment, or a prespecified clinical threshold for an important difference. The registry lists no reported analyses for the secondary outcomes. This limits assessment of whether endpoint definitions, time-to-event methods, censoring, and multiplicity were handled according to a prespecified plan.

The study is described as exploratory Phase II and includes three groups, with modest posted endpoint denominators. The primary comparisons are therefore imprecise, and the observed differences may be sensitive to a small number of outcomes. Open-label assignment could also influence care or outcome assessment, although the registry does not report whether or how outcome assessment was blinded. The primary endpoint's objective criteria do not, by themselves, establish how those criteria were applied.

Safety reporting is aggregated. The record does not explain the timing and attribution of listed deaths or clarify the arm-level basis for the serious adverse event term percentages. These limitations call for cautious interpretation of both efficacy and safety patterns without implying that unreported procedures were necessarily absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dociparstat Sodium (CX-01) Combined With Standard Induction Therapy for Newly Diagnosed Acute Myeloid Leukemia — NCT02873338.
• Registry record last updated 2023-09-07; status last verified 2023-08.
• Results first posted 2021-10-29.
• 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

NCT02873338 is a completed, randomized, open-label, parallel-group Phase II study of dociparstat sodium (CX-01) added to standard induction therapy for newly diagnosed AML. The primary endpoint was the number achieving morphologic complete remission during induction and re-induction. Posted counts were 14 of 26 in control, 8 of 25 with dociparstat 0.125 mg/kg, and 11 of 24 with dociparstat 0.25 mg/kg.

Both primary risk-difference intervals include zero, and the unadjusted p-values are 0.115 and 0.571. The results are uncertain and do not establish a treatment effect. The registry record does not report the original sample-size justification, a formal analysis plan, multiplicity handling, analysis populations, or missing-data methods. Secondary outcomes and safety counts provide descriptive context but do not resolve the primary uncertainty.