To Evaluate Efficacy, Safety, Tolerability and PK of Intravenous Cipargamin in Participants With Severe Plasmodium Falciparum Malaria: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Evaluate Efficacy, Safety, Tolerability and PK of Intravenous Cipargamin in Participants With Severe Plasmodium Falciparum Malaria (NCT04675931), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving at Least 90% Reduction in Plasmodium Falciparum (P. Falciparum) at 12 Hours.

2. Clinical Question

The study also set out to identify a safe and effective intravenous cipargamin dose and to evaluate clinical treatment success using a novel clinical endpoint for drug development in severe malaria. The registry lists a range of secondary outcomes, including clinical success at 48 hours, severe-malaria signs, hemolysis, neurological sequelae, parasite reduction, parasite-clearance measures, and fever-clearance time. These address different aspects of response and safety; they are related but are not interchangeable with the primary 12-hour parasite-reduction measure.

3. Trial Design

This was a phase 2, randomized, active-controlled, sequential-cohort, multicenter study. The official title describes it as open-label and includes adult and pediatric participants with severe Plasmodium falciparum malaria. The registry record classifies masking as single as well as describing the study as open-label; the identity of any masked party is not reported in the registry record. The record lists enrollment as 254 and status as completed.

The three treatment arms were IV cipargamin 20 mg, IV cipargamin 40 mg, and IV artesunate. Participants in each cipargamin arm received at least two intravenous doses 24 hours apart, with no more than 3 doses, followed by oral Coartem twice daily for 3 days. Participants in the artesunate arm received IV artesunate according to label followed by the same stated oral medication schedule. Details about allocation ratios, cohort sequencing decisions, and dose-selection rules are not reported in the registry record.

The primary endpoint was the percentage achieving at least a 90% reduction in P. falciparum at 12 hours. The primary analysis population included randomized participants with baseline parasite count >0 who received at least one dose of intravenous study treatment during the treatment period. The posted arm denominators for this endpoint are 20, 114, and 117 for IV cipargamin 20 mg, IV cipargamin 40 mg, and IV artesunate, respectively. These endpoint denominators are not a substitute for the enrollment figure: analysis populations can be defined by endpoint-specific eligibility and treatment exposure.

The registry lists a study start of 2022-03-07 and primary completion of 2025-07-24. The original sample-size justification, the trial's own statistical analysis plan, and details of any interim analyses are not reported in the registry record. The separate planning illustrations based on observed effects should therefore not be mistaken for the assumptions used to design or conduct this trial.

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: 316 participants were screened for the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set included all randomized participants who had baseline P. falciparum count \>0 and took at least one dose of intravenous study treatment during the treatment 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.

Population: The full analysis set included all randomized participants who had baseline P. falciparum count \>0 and took at least one dose of intravenous study treatment during the treatment period.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving at Least 90% Reduction in Plasmodium Falciparum (P. Falciparum) at 12 Hours, measured over 12 Hours.

The primary endpoint is the percentage of participants who achieved at least a 90% reduction in Plasmodium falciparum at 12 hours. A blood draw was performed at each collection time point for parasitemia assessment. The endpoint turns a laboratory measurement of parasite count into a binary outcome: each participant either met the stated reduction threshold at the specified time point or did not.

A threshold-based outcome is useful for communicating the proportion of participants reaching a defined early response milestone. It also permits a direct comparison of the proportions across randomized groups. However, it does not convey the full trajectory of parasite counts, the magnitude of reduction among participants who cross the threshold, or the time taken to clear parasites. The registry lists time to parasite clearance and a parasite-clearance estimator slope half-life among the secondary outcomes, reflecting distinct ways to characterize that trajectory.

The 12-hour measure is an early biological endpoint, not a complete measure of clinical recovery. The registry separately identifies clinical success at 48 hours and other clinical and safety outcomes. A strong or weak result on the parasite-reduction endpoint therefore should be interpreted as evidence about this specific measure at this specific time, rather than as a summary of all dimensions of benefit or harm.

The full analysis set required randomization, a baseline P. falciparum count >0, and receipt of at least one intravenous study-treatment dose. The registry does not report the detailed handling of missing 12-hour measurements or the precise rule used when an endpoint value was unavailable.

7. Results Posted in the Registry

• IV Cipargamin 40 mg: 93.0% (106/114) versus 80.0% (16/20) on control; risk difference 13.0 percentage points (95% CI -5.2 to 31.1), risk ratio 1.16 (0.93–1.46); unadjusted two-proportion z-test p = 0.061.
• IV Artesunate: 39.3% (46/117) versus 80.0% (16/20) on control; risk difference -40.7 percentage points (95% CI -60.3 to -21.0), risk ratio 0.49 (0.36–0.67); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Participants Achieving Clinical Success at 48 Hours

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • IV Cipargamin 40 mg: 85.1% (97/114) versus 95.0% (19/20) on control; risk difference -9.9 percentage points (95% CI -21.5 to 1.7), risk ratio 0.90 (0.79–1.02); unadjusted two-proportion z-test p = 0.231.
  • IV Artesunate: 74.4% (87/117) versus 95.0% (19/20) on control; risk difference -20.6 percentage points (95% CI -33.0 to -8.2), risk ratio 0.78 (0.68–0.91); unadjusted two-proportion z-test p = 0.041.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IV Cipargamin 40 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for IV Artesunate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several dimensions of response and safety rather than a single unified measure. The registry identifies clinical success at 48 hours, individual signs of severe malaria over time, early and delayed hemolysis, neurological sequelae at Day 29, parasite reduction, parasite-clearance time and slope half-life, and fever-clearance time. Together, these outcomes provide context beyond the primary early parasite-reduction threshold, but each answers a different question.

The posted clinical-success percentages at 48 hours do not follow the same ordering as the primary endpoint percentages: the 20 mg group has the highest reported percentage on this secondary endpoint. This difference in pattern illustrates why results for different endpoints and time points should not be collapsed into a single conclusion. The primary endpoint is a laboratory-based threshold at 12 hours, whereas clinical success at 48 hours is a distinct clinical measure. The registry record does not give a single overall secondary-outcome estimate that combines these results.

The comparison calculations for the secondary clinical-success endpoint are unadjusted. The registry record does not report a multiplicity adjustment, a hierarchy of confirmatory secondary outcomes, or a prespecified rule for interpreting a collection of secondary findings. When many outcomes are examined, some results may appear notable by chance, even when no corresponding underlying difference exists. For that reason, unadjusted secondary p-values carry less weight than a prespecified primary analysis, especially when considered in isolation.

Secondary findings can still be informative: they can show whether the pattern on a primary biological measure is accompanied by a similar or different pattern on clinical outcomes, and they can identify areas requiring further study. They should be interpreted with their own definitions, denominators, intervals, and missing-data handling. The registry does not report enough detail to assess all of those features for every listed secondary outcome, so broad claims across the full set are not warranted from endpoint names alone.

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

• Percentage of Participants Achieving Clinical Success at 48 Hours
• Percentage of Participants With Individual Signs of Severe Malaria Over Time
• Percentage of Participants Developing Hemolysis (Early and Delayed) After Treatment
• Percentage of Participants With Neurological Sequelae at Day 29
• Percentage of Participants Achieving at Least 90% Reduction in Plasmodium Falciparum (P. Falciparum)
• Time to Parasite Clearance (PCT)
• Parasite Clearance Estimator (PCE) Slope Half-life
• Time to Fever Clearance (FCT)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either achieved at least a 90% reduction in P. falciparum by 12 hours or did not. The reported arm values are percentages, and the comparisons use risk differences. A risk difference expresses the difference between two event proportions on the proportion scale. Its sign depends on the order of the groups in the comparison: a positive value means the first stated comparison group has a higher event proportion than the reference group, while a negative value means it has a lower proportion.

The posted primary comparisons are recalculated, unadjusted comparisons based on the summary counts. They are not a substitute for a model-based, covariate-adjusted analysis or for an analysis specified by the sponsor. The registry record does not report a primary comparison analysis or a statistical analysis plan. Because the discrepancy flag is false, no conflict between these recalculations and the posted summaries is identified in the record.

A confidence interval describes a range of estimates compatible with the observed data under the method used. It conveys uncertainty in the estimated effect rather than the range of individual participant outcomes. An interval that includes no difference indicates that the data do not rule out no difference at the corresponding confidence level; it does not show that the groups are identical. Conversely, an interval excluding no difference does not by itself establish clinical importance or prove the result will recur.

The primary endpoint is reported as an arm percentage without a confidence interval in the arm results. The comparison intervals are recalculated from the posted counts. For secondary clinical success, the arm percentages have 90% confidence intervals in the registry results, whereas the comparison intervals are unadjusted recalculations. The different interval sources and confidence levels should not be conflated.

What does an unadjusted p-value say?

A p-value measures how incompatible the observed data are with a specified no-difference model, assuming that model and the test's conditions. It is not the probability that the treatment difference is true, nor does it measure the size or importance of a difference. The primary comparison of 40 mg with 20 mg has p = 0.061; the comparison of artesunate with 20 mg has p < 0.001. Those values address the specific unadjusted comparisons and should be read alongside the estimates and intervals. They do not account for the full set of outcomes and comparisons unless a multiplicity method is used, and adjustment is not reported in the registry record.

Why does the analysis population matter?

The registry defines the primary full analysis set as randomized participants who had baseline P. falciparum count >0 and took at least one dose of intravenous study treatment during the treatment period. This definition sets the population to which the posted primary estimates apply. It is not necessarily identical to all enrolled participants, and it is specific to this endpoint's analysis. The registry does not report details of missing endpoint data, exclusions after randomization, or sensitivity analyses for missingness.

What is the role of the secondary outcomes?

The registry lists 22 secondary outcomes, including clinical success at 48 hours, severe-malaria signs, hemolysis, neurological sequelae, parasite reduction, time to parasite clearance, parasite-clearance slope half-life, and fever-clearance time. These measures address different time points and clinical or laboratory dimensions. For example, a binary threshold at 12 hours asks whether a defined reduction was reached; time-to-clearance outcomes ask how quickly a stated event occurred. Findings across such measures can add context, but they are not interchangeable or necessarily statistically independent.

The clinical-success result at 48 hours is a secondary outcome with posted arm percentages and recalculated comparisons. The other endpoint names establish what the study tracked, but the registry record does not report a single combined secondary summary that can replace outcome-specific interpretation. The registry also lists 23 outcome measures overall. The relationship among outcomes, any prespecified hierarchy, and any formal confirmatory role for the secondary endpoints are not reported in the registry record.

How should the planning calculations be understood?

The separate planning illustrations use two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. The displayed figures are participants per arm for these binary outcomes. They are not the original trial's design calculations, and the original design assumptions are not reported in the registry record. The illustrations do not establish the probability that the completed trial detected an effect; they are planning calculations rather than observed power.

Some design features remain unclear from the registry record. Although the study is described as adaptive and sequential cohort, cohort progression, adaptation criteria, interim decision rules, and any effect of those features on the inferential analysis are not reported in the registry record. Allocation concealment, the identity of any masked party, and detailed model specifications are likewise not reported. These gaps limit independent assessment of the exact analytic procedures, but do not alter the basic reading of the posted proportions, estimates, and intervals.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate an effect estimate. Narrower confidence intervals indicate more precise estimates under the analysis method; wider intervals indicate greater uncertainty. A confidence interval is not a guarantee that the true value lies inside it, and it does not describe the range of responses among individual participants.

For the primary comparison of IV cipargamin 40 mg with IV cipargamin 20 mg, the recalculated risk difference is 0.130, with an interval from -0.052 to 0.311. The interval spans no difference and includes estimates on either side. This leaves substantial uncertainty about the direction and magnitude of the difference. The comparison has a 20-participant denominator in the 20 mg arm and a 114-participant denominator in the 40 mg arm, so the smaller reference group is relevant when considering the amount of information behind the estimate.

For IV artesunate compared with IV cipargamin 20 mg, the recalculated risk difference is -0.407, with an interval from -0.603 to -0.210. This interval excludes no difference, while still allowing a range of possible magnitudes. As with any interval, it reflects sampling uncertainty under the calculation and does not settle clinical importance or external applicability.

The arm-level primary percentages are not accompanied by reported confidence intervals in the registry results. Their apparent separation should therefore be read with the denominators and the recalculated comparison intervals, rather than as exact population values. For the secondary clinical-success endpoint, the registry reports 90% confidence intervals for each arm: 78.4 to 99.7 for IV cipargamin 20 mg, 78.5 to 90.3 for IV cipargamin 40 mg, and 66.9 to 80.9 for IV artesunate. The confidence level differs from a conventional 95% interval, so those intervals should not be compared as if they had the same coverage level.

In general, estimates from smaller groups tend to be less precise than estimates from larger groups, all else equal. That general principle helps explain why the denominator matters, but it does not determine the interval by itself. The posted interval calculations, endpoint definition, and analysis method also matter. The registry record does not report adjusted intervals for the primary result or additional precision analyses.

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 display translates an observed difference into illustrative sample sizes for future two-arm studies. For these binary endpoints, the entries are participants per arm, not totals across both arms. The 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 original sample-size assumptions used to design this trial are not reported in the registry record.

For each effect assumption, the 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting an effect of that size under the stated assumptions, if that effect and those assumptions were correct. The 90% power column uses a higher target probability of detecting the specified effect, and therefore generally calls for a larger planned group. These are prospective planning quantities, not guarantees about a future result.

The rows describe planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants per arm as the effect being targeted becomes smaller. The observed effect is only one estimate from this trial and may not be the effect seen in another study. The calculations are therefore best read as scenario comparisons: they show how the estimated planning requirement changes when the assumed effect is reduced, while holding the listed assumptions fixed.

These figures are not observed power. They do not describe the probability that the completed trial detected its true effect, and they do not establish that a planned sample would produce a particular result. The sample-size illustration is separate from the study's enrollment and endpoint denominators; it should not be read as a report of the trial's original design rationale.

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 = 0.800; treatment proportion p₁ = 0.930; average p̄ = 0.865.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4834 = 0.9475.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4746 = 0.3994.
4. n = (0.9475 + 0.3994)² / (0.1298)² = 107.6, rounded up to 108 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 <- 0.8                          # control proportion
p1 <- 0.929824561403509                          # 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(4675931)
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 = 108 (80% power), 144 (90% power)
 75% of observed effect: n per arm = 212 (80% power), 283 (90% power)
 50% of observed effect: n per arm = 519 (80% power), 694 (90% power)
power.prop.test: 107.6 
Simulated power at n = 108 per arm: 0.824 (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 22 secondary outcomes, and the record describes multiple treatment arms. Considering multiple endpoints and comparisons creates a multiplicity issue: the more statistical tests examined, the greater the chance that at least one result will look noteworthy by chance. A prespecified testing hierarchy or an adjustment can help control that problem, but multiplicity handling is not reported in the registry record. The posted comparison p-values should therefore be understood as unadjusted and outcome-specific, not as evidence that a family of outcomes has been confirmed.

The registry defines the primary full analysis set as all randomized participants with baseline P. falciparum count >0 who took at least one dose of intravenous study treatment during the treatment period. That definition is important because the reported primary percentages apply to this analysis population. The record does not report a separate intention-to-treat analysis, a per-protocol analysis, or how many randomized participants were excluded from the primary analysis for each reason.

Missing-data handling is not reported in the registry record. In particular, the record does not describe how participants without a 12-hour parasite measurement were handled, whether any values were imputed, or whether sensitivity analyses assessed alternative assumptions about missing outcomes. Missingness can affect an estimate if participants with unavailable measurements differ systematically from those with observed measurements. Without the analysis details, the possible influence cannot be quantified.

The primary comparison intervals and p-values are unadjusted recalculations from posted summary statistics. The registry record does not provide a detailed model specification, covariate adjustment plan, or analysis code. It also does not report the original sample-size justification or the statistical consequences of the adaptive, sequential-cohort design. These omissions do not negate the posted arm percentages, but they limit assessment of whether all design features and analysis decisions were incorporated into formal inference.

Finally, the registry lists masking as single while the official title describes the trial as open-label. The identity of any masked party and how masking was maintained are not reported in the registry record. These reporting gaps should be kept separate from the observed numerical results: they affect how fully the analysis can be evaluated, rather than changing what the posted summaries state.

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: malaria (1.8%), anaemia (1.7%), hepatic function abnormal (0.9%), seizure (0.9%), thrombocytopenia (0.9%).

The registry reports serious adverse events among participants at risk by treatment group. Serious adverse events affected 0 of 20 participants in the IV cipargamin 20 mg group, 5 of 114 in the IV cipargamin 40 mg group, and 4 of 117 in the IV artesunate group. The total row reports 9 affected among 251 at risk. Deaths are reported as 0 in each group and in the total row.

Other adverse events affected 7 of 20 participants in the 20 mg group, 57 of 114 in the 40 mg group, and 50 of 117 in the artesunate group; the total row reports 114 affected among 251 at risk. The listed serious adverse-event terms include Malaria at 1.8%, Anaemia at 1.7%, and Hepatic function abnormal, Seizure, Thrombocytopenia, and Haemoglobin decreased at 0.9% each.

These counts are descriptive. They do not establish that a treatment caused an event, and the record does not provide comparative safety estimates or confidence intervals for these counts. The total row is the registry's reported safety summary; it should not be treated as a randomized comparison. Seriousness and causal attribution are distinct: the registry's listed figures identify serious events and affected participants, but the event counts alone do not establish treatment-relatedness.

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

The posted results describe how often participants in each randomized group reached the primary 12-hour parasite-reduction threshold and the secondary 48-hour clinical-success outcome. On the primary measure, the reported percentage was 93.0% in the IV cipargamin 40 mg group and 39.3% in the IV artesunate group, with 80.0% in the IV cipargamin 20 mg group. The recalculated comparisons quantify the observed differences and their uncertainty. They are evidence about these study groups and these endpoint definitions, not a complete account of treatment effects.

The primary comparison between cipargamin doses is uncertain: its recalculated interval includes no difference. The comparison between artesunate and the 20 mg arm has an interval that excludes no difference, but the interval still allows a range of effect sizes. Neither result alone says how clinically important the observed difference is. Statistical evidence, effect magnitude, endpoint relevance, and study limitations all matter to interpretation.

The result does not establish that one regimen is best for every participant, nor does it answer all questions about clinical recovery. The primary endpoint is an early parasite-count threshold, while clinical success is a separate secondary outcome. Other listed endpoints include safety and later clinical measures. The registry does not provide a single summary that resolves every aspect of benefit and harm.

The study's randomized, active-controlled design supports comparisons among its assigned groups, but the record leaves important details unreported, including the original design assumptions, missing-data procedures, multiplicity handling, and the statistical analysis plan. The sequential-cohort and adaptive features are described in the title, but the operational and inferential details are not reported in the registry record.

Accordingly, the posted numbers should be read as study findings with stated denominators and uncertainty, not as medical advice or a general treatment recommendation. Applicability to other populations, settings, or treatment practices is not established by these registry results alone. The record describes a completed phase 2 study; it does not by itself answer what further evidence may be needed or how these findings should guide individual care.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it compares a binary early parasite-reduction endpoint across two cipargamin dose groups and an active comparator, while also tracking clinical and safety outcomes. The primary endpoint is concrete and time-specific: whether participants reached at least a 90% reduction in P. falciparum by 12 hours. Such thresholds can make results easy to communicate, but they compress a continuous biological trajectory into a yes-or-no classification. The registry's other parasite-clearance measures address aspects of that trajectory that a threshold alone cannot capture.

The randomized design gives the comparisons a stronger basis than an uncontrolled description of outcomes, but precision still depends on the information in each group. The 20 mg group has a smaller posted primary endpoint denominator than the other arms, and its comparison interval reflects uncertainty. The reported arm percentages should be considered alongside the risk-difference estimates and intervals rather than interpreted as exact values for a wider population.

The study also demonstrates why endpoint selection matters. The primary biological measure and the secondary clinical-success outcome show different group patterns. A laboratory response at an early time point is not identical to clinical success later, and statistical evidence on one does not automatically establish the other. Multiple endpoints can provide a richer account, but without reported multiplicity procedures their unadjusted tests require cautious interpretation.

Finally, the registry's description of an adaptive, sequential-cohort study raises design questions that cannot be fully evaluated from the record because adaptation rules and their analysis implications are not reported. The posted data remain interpretable as arm-level summaries and unadjusted comparisons, while the missing design and analysis detail limits independent reconstruction of the full inferential approach.

18. Limitations

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

Several limitations specific to this trial affect interpretation. The study is described as adaptive and sequential cohort, but the rules for cohort progression, dose decisions, interim review, or adaptation are not reported in the registry record. Without those details, it is not possible to assess how the sequential design may have influenced allocation, stopping, or the interpretation of estimates.

The record gives no original sample-size justification or detailed statistical analysis plan. The planning illustrations based on observed effects are not evidence of the trial's original design assumptions. The primary result is reported as percentages, while its comparison estimates and intervals are recalculated from posted summary counts. The registry does not report a sponsor analysis to compare with those calculations.

The primary endpoint is a thresholded parasite-reduction measure at 12 hours. It does not capture the complete parasite trajectory or all dimensions of clinical response. The separate clinical-success measure at 48 hours and the other secondary outcomes address different questions, and multiplicity handling for the outcome set is not reported. This makes isolated secondary p-values less definitive.

The primary analysis population has a defined treatment-exposure and baseline-count requirement, but the registry does not report detailed reasons for exclusions or the handling of missing endpoint measurements. Missing-data sensitivity analyses are not reported. The record also does not identify who, if anyone, was masked, despite describing the trial as open-label and classifying masking as single.

Finally, the posted results are from a phase 2 study in adult and pediatric participants with severe malaria. The registry record does not establish how well the findings generalize to populations, settings, or clinical circumstances not represented by the study. These reporting and design limitations do not erase the observed summaries, but they constrain the strength and breadth of conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: To Evaluate Efficacy, Safety, Tolerability and PK of Intravenous Cipargamin in Participants With Severe Plasmodium Falciparum Malaria — NCT04675931.
• Registry record last updated 2026-04-09; status last verified 2026-03.
• Results first posted 2026-04-09.
• 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

NCT04675931 is a completed phase 2 randomized, active-controlled, multicenter study of IV cipargamin and IV artesunate in adult and pediatric participants with severe Plasmodium falciparum malaria. The primary endpoint was the percentage achieving at least a 90% reduction in P. falciparum at 12 hours. The registry reports arm percentages of 80.0% for IV cipargamin 20 mg, 93.0% for IV cipargamin 40 mg, and 39.3% for IV artesunate.

The study also reports clinical success at 48 hours as a secondary outcome, alongside additional clinical, parasite-clearance, and safety measures. The posted unadjusted comparisons and recalculated intervals indicate uncertainty that should be considered with the arm denominators and endpoint definitions. Multiplicity handling, missing-data procedures, detailed adaptive-design rules, and the original sample-size assumptions are not reported in the registry record.