A Dose Finding, Efficacy and Safety Study of Ensovibep (MP0420) in Ambulatory Adult Patients With Symptomatic COVID-19: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Dose Finding, Efficacy and Safety Study of Ensovibep (MP0420) in Ambulatory Adult Patients With Symptomatic COVID-19 (NCT04828161), a randomized phase 2, phase 3 study. The primary outcome is Part A: Time-Weighted Change From Baseline in Log10 Severe Acute Respiratory Syndrome Coronavirus 2 (SARS-CoV-2) Viral Load Through Day 8.

2. Clinical Question

3. Trial Design

The registry describes NCT04828161, the EMPATHY trial, as a randomized, double-blind, placebo-controlled, multicenter, parallel-group study. It lists Phase 2 and Phase 3. The study enrolled 407 participants and is recorded as terminated. The start date was 2021-05-10 and the primary completion date was 2021-11-18. These dates describe the registry record and do not explain why the study was terminated.

Part A was the dose-finding component represented in the posted primary endpoint results. It included ensovibep 75 mg, 225 mg, and 600 mg arms and a placebo arm. The registry lists a Phase 3 Part B, but explicitly states that Part B was not initiated. The results discussed for the primary endpoint therefore concern Part A, not a completed Phase 3 comparison.

The primary outcome was time-weighted change from baseline in log10 SARS-CoV-2 viral load through Day 8, using measurements at baseline and Days 3, 5 and 8. Posted group results are available for 89 participants in the 600 mg arm, 97 in the 225 mg arm, 97 in the 75 mg arm, and 87 in the placebo arm. These are endpoint analysis counts, not a reconciliation of the overall enrollment figure.

The registry lists 18 outcome measures and 3 analyses, while the posted secondary outcome list includes measures of COVID-19 hospitalization and/or emergency-room visits or death, time to sustained clinical recovery, and pharmacokinetic measures of ensovibep. Results for all listed outcomes are not included in the registry record used for this explanation. The trial’s planned sample-size justification, original statistical assumptions, and reasons for termination 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: The Part A of the study consisted of a screening period (up to 3 days) followed by study treatment on Day 1. Participants were randomized in 1:1:1:1 ratio, stratified by risk for COVID-19 disease progression, to receive 1 of 4 study treatments (Ensovibep 600 mg or Ensovibep 225 mg or Ensovibep 75 mg or Placebo). A total of 407 participants were randomized in the study, of which 400 were treated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The FAS included all participants in the randomized set for whom IV infusion of study treatment was administered. Only participants included in the analysis are reported.

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: Full analysis set (FAS) included all participants in the randomized set for whom IV infusion of study treatment was initiated during the treatment period.

6. Primary Endpoint

The registry lists the primary outcome as Part A: Time-Weighted Change From Baseline in Log10 Severe Acute Respiratory Syndrome Coronavirus 2 (SARS-CoV-2) Viral Load Through Day 8, measured over Baseline (Day 1) and Days 3, 5 and 8.

The primary endpoint is the time-weighted change from baseline in log10 SARS-CoV-2 viral load through Day 8. Viral load was measured from nasopharyngeal swabs using quantitative reverse transcription-polymerase chain reaction at a central laboratory. The scheduled measurements were at baseline (Day 1) and Days 3, 5 and 8.

Viral load is a continuous laboratory measure of the amount of viral material detected in a sample. Expressing it on a log10 scale represents changes multiplicatively on the original scale, while the reported endpoint compares changes on the logarithmic scale. A negative change indicates a reduction relative to baseline. In these results, the arm-level least-squares means are negative in both ensovibep and placebo groups.

The endpoint is time-weighted because measurements were collected at multiple time points rather than at a single follow-up visit. In general, a time-weighted summary can represent the pattern across scheduled measurements, instead of giving exclusive emphasis to one measurement. The registry record does not provide the precise weighting formula.

A viral-load endpoint can address antiviral activity over the specified follow-up period. It does not by itself establish what participants experienced in terms of symptoms, recovery, hospital care, or other clinical outcomes. Those questions require their own outcome results. The registry lists several secondary outcomes related to clinical events and recovery, but their results are not reported in the registry record used for this analysis.

7. Results Posted in the Registry

• Ensovibep 600 mg: mean -1.99 versus -1.40 on control; difference -0.59 (95% CI -0.86 to -0.32), standardized effect d = -0.65; z-test p = <0.001.
• Ensovibep 225 mg: mean -1.73 versus -1.40 on control; difference -0.33 (95% CI -0.59 to -0.07), standardized effect d = -0.36; z-test p = 0.015.
• Ensovibep 75 mg: mean -1.81 versus -1.40 on control; difference -0.41 (95% CI -0.67 to -0.15), standardized effect d = -0.45; z-test p = 0.002.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: it is a numerical measure of change in viral load rather than a count of events or a time until an event. The registry identifies the reported group values as least-squares means and their dispersion as standard errors. A least-squares mean is a model-based estimate of a group mean, potentially adjusted for terms in the analysis model. The precise covariates and model specification are not reported in the registry record.

What does the ANCOVA comparison represent?

The sponsor reports comparisons using ANCOVA and labels the results as LS mean differences. In general, analysis of covariance estimates group differences while accounting for selected covariates included in the model. This can make the comparison differ from a simple subtraction of group summaries. The registry record does not identify the covariates, any stratification factors, or the details of model fitting. The sponsor’s estimates are therefore the primary reported inferential results, rather than the simpler recalculations based on the posted arm summaries.

For the sponsor’s analysis, the 600 mg versus placebo LS mean difference is -0.59, with a 95% confidence interval from -0.86 to -0.32 and p < 0.001. For 225 mg versus placebo, the difference is -0.33, with a 95% confidence interval from -0.60 to -0.07 and p = 0.014. For 75 mg versus placebo, it is -0.42, with a 95% confidence interval from -0.68 to -0.15 and p = 0.002. The negative signs indicate that the estimated time-weighted change was more negative in the ensovibep arm than in placebo under the sponsor’s analysis.

Why are there also recalculated results?

The unadjusted recalculations use the posted arm-level estimates and standard errors to approximate a pooled standard deviation and compare each active arm with placebo. They are simple checks based on summary statistics, not a reproduction of the sponsor’s ANCOVA model. The standard deviations are marked as approximate because they are inferred from standard errors rather than taken from directly reported group-level standard deviations. The recalculations also do not incorporate unreported model covariates or other features of the sponsor’s analysis.

Consequently, the recalculated and sponsor-reported values can differ. The 75 mg difference is -0.41 in the recalculation and -0.42 in the sponsor’s analysis; for 225 mg, the recalculated p-value is 0.015 while the sponsor reports 0.014. These are not evidence that either result was entered incorrectly: they arise from analyses with different inputs and methods. Where a discrepancy is flagged, the sponsor’s own analysis takes precedence.

How should p-values be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the statistical model. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. Small p-values do not remove uncertainty about the estimate, which is why confidence intervals are also informative. The sponsor’s reported p-values are comparisons of each dose with placebo; the registry record does not say whether these p-values were adjusted for the multiple dose comparisons.

Multiplicity arises when several hypotheses are tested within a study. In general, making multiple comparisons can increase the chance of at least one false-positive finding if each is interpreted without an appropriate strategy. The registry describes a multiple comparison procedure-modeling methodology for the endpoint, but the posted description does not specify the precise procedure or its relationship to the posted ANCOVA comparisons. No claim about multiplicity adjustment can be made from the available details.

What is the role of the endpoint population?

The registry describes the FAS as participants in the randomized set for whom IV infusion of study treatment was administered. It also says only participants included in the analysis are reported. The arm-specific analyzed counts are 89, 97, 97, and 87 for 600 mg, 225 mg, 75 mg, and placebo, respectively. The registry entries do not identify the number of randomized participants who did not enter this analysis, the reasons for any exclusions, or how missing viral-load measurements were handled.

In general, missing outcome data can affect the interpretation of an analysis, especially if the probability of missingness is related to participants’ outcomes or treatment group. Methods may include assumptions or models for incomplete measurements, but the registry record does not report the missing-data approach for this endpoint. It also does not report sensitivity analyses assessing the effect of missing data.

Why can variability matter?

The posted arm-level dispersion is a standard error, which describes uncertainty in an estimated mean. It is not the same as the spread of individual participant measurements. In general, the standard error depends on both individual-level variability and the amount of information available. The approximate recalculation infers a pooled standard deviation from the standard errors and analysis counts; this is why it is described as approximate. Greater variability among participants can make a group comparison less precise, while a larger analysis population can improve precision when other conditions are similar.

10. Confidence Intervals and Precision

A confidence interval gives a range of values compatible with the data and the assumptions of the analysis at its stated confidence level. It conveys uncertainty around an estimated difference, rather than a guarantee that the true value lies in the interval. The sponsor reports 95% confidence intervals for all three comparisons with placebo.

For ensovibep 600 mg, the sponsor’s estimated difference is -0.59 and the 95% confidence interval runs from -0.86 to -0.32. For 225 mg, the estimate is -0.33 and the interval runs from -0.60 to -0.07. For 75 mg, the estimate is -0.42 and the interval runs from -0.68 to -0.15. Each interval is entirely on the negative side of zero. Under the sponsor’s reported model, the data therefore support a negative difference for each comparison at the stated confidence level. The intervals still allow a range of possible magnitudes, and they do not indicate the clinical importance of those magnitudes.

The endpoint arm estimates have standard errors of 0.097 for the 600 mg arm, 0.093 for 225 mg, 0.093 for 75 mg, and 0.098 for placebo. Standard errors describe precision of the estimated means, not the full spread of individual viral-load changes. Precision for a contrast also depends on the model and the uncertainty in both groups being compared.

Approximate recalculated intervals are not identical to the sponsor’s ANCOVA intervals. For example, the recalculated 75 mg interval is -0.675 to -0.145, while the sponsor reports -0.68 to -0.15. Because the recalculation uses approximate dispersion and does not reproduce the sponsor’s model, the sponsor’s reported interval is the relevant one for interpreting the sponsor’s analysis. The registry record does not report confidence intervals for the arm-level means themselves.

11. 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 figures are illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous-outcome comparisons, the figures are participants per arm, not total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects equal to the stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives 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 its assumptions. The 90% power column gives the corresponding number per arm for a higher chance of detection. Power is a property of a planned study under assumptions; it is not a probability that a particular result is true.

The rows describe planning for 100%, 75%, or 50% of the observed effect. As the effect to be detected gets smaller, more participants are needed to distinguish it from random variation with the same planned power and significance level. For the 600 mg comparison, the illustration gives 38 participants per arm for 80% power and 51 for 90% power when planning for 100% of the observed effect; the figures rise to 151 and 202 when planning for 50% of the observed effect. The same principle applies to the other dose comparisons, though the specific figures differ because the observed estimates differ.

These are not observed power calculations for the completed trial. They are prospective planning illustrations using the observed effects as inputs, and their assumptions may not match the sponsor’s original design.

12. 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.590; pooled standard deviation σ = 0.915.
2. n = 2 × (1.96 + 0.842)² × 0.915² / -0.590² = 37.7, rounded up to 38 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
delta <- -0.59                      # observed difference in means
sigma <- 0.914595620711846                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4828161)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 38 (80% power), 51 (90% power)
 75% of observed effect: n per arm = 68 (80% power), 90 (90% power)
 50% of observed effect: n per arm = 151 (80% power), 202 (90% power)
power.t.test: 38.7 
Simulated power at n = 38 per arm: 0.793 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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.

13. Analyses Reported by the Sponsor

The sponsor’s reported results use ANCOVA and give LS mean differences, 95% confidence intervals, and p-values. The recalculated results are simple unadjusted comparisons derived from the posted arm estimates and standard errors, with approximate pooled standard deviations. They answer a related but not identical statistical question, because the recalculation cannot reproduce unreported parts of the sponsor’s model.

The results are broadly close, but not exactly the same. For 600 mg, the recalculated difference is -0.59, matching the sponsor’s reported -0.59 at the displayed precision. For 225 mg, both differences are -0.33, while the recalculated p-value is 0.015 and the sponsor reports 0.014. For 75 mg, the recalculated difference is -0.41, compared with the sponsor’s -0.42; the p-values are 0.002 in both analyses. The recalculated intervals also differ slightly from the sponsor’s intervals.

These differences are expected when an approximate unadjusted calculation is compared with a model-based analysis. The recalculation is useful as a transparent check on the scale and direction of the posted summaries, but it should not be treated as a substitute for the prespecified or sponsor-reported analysis. Given the flagged discrepancy, the sponsor’s own analysis takes precedence. The registry record does not provide enough model detail to identify exactly which analytic choices account for each difference.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint compares three ensovibep dose arms with placebo. Multiple comparisons raise a general multiplicity issue: interpreting several tests independently can increase the chance of a false-positive result across the family of comparisons. The registry description says a multiple comparison procedure-modeling methodology was used for the primary endpoint. However, the record does not explain the procedure, identify the testing hierarchy, or state whether the posted ANCOVA p-values and confidence intervals incorporate multiplicity adjustment. The unadjusted recalculations do not adjust for multiple comparisons.

The sponsor’s posted p-values are p < 0.001 for 600 mg, 0.014 for 225 mg, and 0.002 for 75 mg. They should be read as reported for the stated comparisons, without assuming an adjustment that is not described. The registry record does not report interim analyses, stopping rules, or the statistical plan in sufficient detail to establish how the family of hypotheses was handled.

The analysis population is described as the FAS, including randomized participants who received an IV infusion of study treatment. The record says only participants included in the analysis are reported. It does not give a complete account of participant flow into the endpoint analysis or explain any differences between randomized, treated, and analyzed participants.

Missing-data handling is also not reported in the registry record. The endpoint was measured repeatedly through Day 8, but the record does not state how missing scheduled swabs or other incomplete measurements were treated, what assumptions were made, or whether sensitivity analyses were performed. In general, the implications of missing data depend on why measurements are absent and on the method used to analyze the available observations. Without those details, the robustness of the endpoint estimates to missing measurements cannot be assessed from the registry information alone.

The record does not report the trial’s original sample-size justification, planned interim analyses, or detailed statistical analysis plan. These gaps limit assessment of the intended testing strategy and the relationship between the posted analysis and the original protocol.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 pneumonia (4.0%), septic shock (2.0%), covid-19 (1.0%), angina pectoris (1.0%), cor pulmonale (1.0%).

The posted safety figures report serious adverse events among participants at risk in each group. There were 0 serious adverse events among 100 participants at risk in the 600 mg arm, 2 among 98 in the 225 mg arm, and 1 among 102 in the 75 mg arm. The ensovibep total is reported as 3 among 300 at risk. In the placebo group, 9 serious adverse events were reported among 100 at risk. These are descriptive counts; the registry record does not provide a comparative safety analysis or confidence intervals for these figures.

The record lists COVID-19 pneumonia, septic shock, COVID-19, angina pectoris, cor pulmonale, and hiatus hernia among the serious adverse-event terms, with reported percentages of 4.0%, 2.0%, 1.0%, 1.0%, 1.0%, and 1.0%, respectively. The registry entries do not explain the event coding, whether participants could contribute more than one event, or how these terms map to the group-level counts.

Deaths are reported as 0 in each ensovibep dose arm and 2 in the placebo arm. The figures describe what was posted for the study and do not establish a causal relationship between treatment and any event. The registry record does not report enough detail about event timing, exposure duration, adjudication, or comparative safety methods to support broader conclusions.

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

The primary result concerns a laboratory measure of SARS-CoV-2 viral load over the period through Day 8. The sponsor’s ANCOVA estimates are negative for each ensovibep dose compared with placebo, and each reported 95% confidence interval lies below zero. The posted data therefore indicate estimated differences in the direction of a greater reduction in the ensovibep groups on this endpoint. This is a statistical description of the measured outcome, not a conclusion about treatment benefit.

Viral load is not interchangeable with how quickly a participant feels recovered or whether a participant experiences hospitalization, an emergency-room visit, or death. The registry lists secondary outcomes covering some of these clinical events and recovery, but the registry entries used do not include their results. The primary endpoint alone cannot establish effects on those outcomes, nor does it show how long any viral-load difference might persist beyond the specified follow-up.

The endpoint estimates also do not establish an optimal dose. The arm estimates are not strictly ordered by dose: 75 mg has a more negative reported arm mean than 225 mg, while 600 mg has the most negative value. This pattern does not establish a dose-response relationship, and the registry record does not report a formal dose-trend analysis or the basis for selecting an optimal dose.

The study is recorded as terminated, and Phase 3 Part B was not initiated. Those details are relevant to the scope of the available evidence: the posted primary results concern Part A, rather than a completed Part B evaluation. The reason for termination is not reported in the registry record. The posted findings should therefore be understood as estimates from the analyzed Part A population and endpoint, with the uncertainty and reporting gaps.

More generally, statistical significance is not a measure of clinical importance. A confidence interval and p-value describe the evidence under an analysis model; neither establishes that an observed difference matters to patients. The registry record does not supply a threshold for a clinically meaningful viral-load change, so the clinical importance of these estimated differences cannot be determined from the primary endpoint results alone.

17. Why This Trial Matters Statistically

This trial is statistically informative because it reports a continuous, repeatedly measured virologic endpoint across several dose arms and a placebo group. The time-weighted summary uses measurements collected at baseline and scheduled follow-up visits, while the sponsor’s analysis reports model-based contrasts with confidence intervals. Together, these results illustrate how an endpoint estimate, its uncertainty, and a model-based comparison answer related but distinct questions.

The record also makes a useful distinction between a sponsor-reported analysis and an approximate recalculation from summary statistics. Recalculations can help readers check the direction and approximate scale of results, but they cannot reproduce a model when relevant details are not reported. Here, small differences between the two analyses reinforce the importance of giving priority to the sponsor’s ANCOVA results and describing the recalculation as approximate.

Multiplicity is a key interpretive issue because the primary endpoint is compared across three dose arms. The record mentions a multiple comparison procedure-modeling methodology but does not explain how it relates to the posted p-values. This illustrates why a method label alone is not enough to assess family-wise inference: readers need the procedure and its application to the reported comparisons.

The study’s status and design history also matter. Although the record lists Phase 2 and Phase 3, it states that Part B was not initiated and records the study as terminated. The available primary results therefore answer a narrower question than a completed multi-part development program might have answered. The record does not report the reason for termination or the original sample-size rationale.

Finally, the endpoint is virologic, while the listed secondary outcomes include clinical events and recovery. Keeping those outcome types distinct prevents a statistical result on viral load from being overextended into an unsupported clinical claim.

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 primary endpoint is limited to a virologic measure through Day 8. The registry record does not report a clinically meaningful threshold for the measure, so the practical importance of the estimated differences cannot be judged from the endpoint alone. Nor do the primary results establish effects on recovery, hospitalization, emergency-room visits, or mortality; results for the listed secondary outcomes are not reported in the registry record used.

Part B was not initiated, and the study is recorded as terminated. The reason for termination is not reported in the registry record. Consequently, the findings described are from Part A and should not be interpreted as results from a completed Phase 3 component. The registry lists both Phase 2 and Phase 3, but this does not mean that both components generated results.

Important analysis details are absent. The record does not provide the full ANCOVA specification, the covariates, the precise multiple-comparison procedure, or an explanation of how it relates to the posted comparisons. It also does not report the missing-data method, sensitivity analyses, interim analyses, or original sample-size justification. These omissions restrict evaluation of model assumptions and robustness.

The recalculated comparisons are approximate and unadjusted, using dispersion inferred from standard errors. They cannot replace the sponsor’s model-based analyses, and the reported discrepancy makes that distinction especially important. Safety figures are descriptive counts without a reported comparative analysis, and available information does not establish causal attribution for adverse events. Overall, interpretation is constrained to the specific posted endpoint, analyzed groups, and registry entries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Dose Finding, Efficacy and Safety Study of Ensovibep (MP0420) in Ambulatory Adult Patients With Symptomatic COVID-19 — NCT04828161.
• Registry record last updated 2026-01-27; status last verified 2026-01.
• Results first posted 2023-01-18.
• 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

NCT04828161, the EMPATHY trial, is recorded as a randomized, double-blind, placebo-controlled, multicenter, parallel-group study of ensovibep in ambulatory adults with symptomatic COVID-19. The registry lists Phase 2 and Phase 3, enrollment of 407, and terminated status. Part A compared ensovibep 75 mg, 225 mg, and 600 mg with placebo; Phase 3 Part B was not initiated.

The primary endpoint was time-weighted change from baseline in log10 SARS-CoV-2 viral load through Day 8, measured at baseline and Days 3, 5 and 8. The sponsor reported negative LS mean differences versus placebo for all dose comparisons, with 95% confidence intervals below zero. Approximate unadjusted recalculations are similar but not identical, so the sponsor’s own analysis takes precedence.

The record does not report the reason for termination, the original sample-size justification, detailed multiplicity handling, or missing-data methods. The viral-load findings do not by themselves establish clinical benefit or effects on the listed secondary outcomes.