MP0420 for Inpatients With COVID-19 (An ACTIV-3/TICO Treatment Trial): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for MP0420 for Inpatients With COVID-19 (An ACTIV-3/TICO Treatment Trial) (NCT05780463), a randomized phase 3 study. The primary outcome is Number of Participants With Sustained Recovery.

2. Clinical Question

The comparison concerns an outcome defined by a sequence of events, not simply discharge on a particular day. Sustained recovery required discharge from the index hospitalization, followed by being alive and at home for 14 consecutive days before Day 90. The endpoint therefore combines a hospital-discharge milestone with a subsequent period at home while alive.

The registry record describes a Phase 3, randomized, blinded, parallel-group study. Its brief summary frames the investigation as an evaluation of the safety and effectiveness of MP0420 in hospitalized people with COVID-19. The comparison is between two treatment strategies that both included standard of care; it is not a comparison of MP0420 alone against no treatment. Remdesivir was part of standard care unless contraindicated, rather than the distinguishing randomized treatment.

The central statistical question is whether the observed proportion meeting the sustained-recovery definition differed between the assigned groups, and how precisely that difference was estimated. The posted results describe the groups and an unadjusted risk-difference estimate. They do not establish why an individual participant did or did not meet the endpoint.

3. Trial Design

The registry record identifies NCT05780463 as a Phase 3 randomized trial of MP0420 for hospitalized patients with COVID-19, conducted within the ACTIV-3/TICO Treatment Trial. Its official title describes a multicenter, adaptive, randomized, blinded controlled trial, and the record labels this investigation Trial H5: MP0420. The recorded design model is parallel group, with triple masking.

The two assigned groups were MP0420 plus standard of care and placebo plus standard of care. The MP0420 arm description specifies a 600 mg solution administered by intravenous infusion. The placebo was also administered by intravenous infusion. Remdesivir was provided to participants as standard of care unless it was contraindicated for an individual patient. Thus the randomized contrast was the addition of MP0420 versus placebo on a background of standard care, not the presence versus absence of all treatment.

The registry record lists enrollment of 485. The arm-level results list 247.0 participants in the MP0420-plus-standard-of-care group and 238.0 in the placebo-plus-standard-of-care group. The sponsor is the National Institute of Allergy and Infectious Diseases (NIAID). The recorded study start date is 2021-06-11, the primary completion date is 2022-02-23, and the status is completed.

The official title uses the term adaptive, but the specific adaptive features, any interim analyses, and the rules for any design changes are not reported in the registry record. The roles included in triple masking and the trial's detailed allocation procedures are also not reported in the registry record. The original sample-size justification and the original design assumptions are not reported in the registry record. The planning illustrations associated with the posted results are separate from those original design details.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Sustained Recovery, measured over Through Day 90.

The primary endpoint counts participants with sustained recovery through Day 90. The registry definition requires discharge from the index hospitalization, followed by being alive and at home for 14 consecutive days before Day 90. A participant must meet this sequence to count as having sustained recovery; discharge alone is not the complete definition.

This endpoint is used to represent a recovery state that extends beyond the immediate hospital-discharge event. Requiring a period alive and at home makes the outcome sensitive to whether discharge is followed by a sustained interval outside hospital. In general, a composite or sequential endpoint can capture more of a participant's clinical course than a single momentary status, although its interpretation depends on the exact definition and follow-up.

The outcome is recorded as a count of participants, with the group sizes serving as the denominators for the comparison. The posted results give 203.0 participants with sustained recovery among 247.0 in the MP0420-plus-standard-of-care group, and 190.0 among 238.0 in the placebo-plus-standard-of-care group. The accompanying risk-difference estimate compares the groups' observed proportions.

The definition does not indicate how events occurring after Day 90 were handled, nor does the registry record explain procedures for participants whose recovery status could not be determined. Those details are not reported in the registry record. The endpoint should therefore be read according to its stated Day 90 definition rather than as a complete account of longer-term health.

7. Results Posted in the Registry

• Placebo Plus SOC: 79.8% (190/238) versus 82.2% (203/247) on control; risk difference -2.4 percentage points (95% CI -9.3 to 4.6), risk ratio 0.97 (0.89–1.06); unadjusted two-proportion z-test p = 0.509.

8. Secondary Efficacy Endpoints

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

Number of Participants Who Died From All Causes

• 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:
  • Placebo Plus SOC: 14.7% (35/238) versus 12.1% (30/247) on control; risk difference 2.6 percentage points (95% CI -3.5 to 8.6), risk ratio 1.21 (0.77–1.91); unadjusted two-proportion z-test p = 0.408.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo Plus SOC and the control. The interval gives the range of effects that remain compatible with the data.

The registry record identifies mortality through Day 90 and several safety outcomes at specified follow-up times as secondary outcomes. Their role is to add context to the primary sustained-recovery comparison, not to redefine its result. Mortality and safety outcomes address different aspects of participants' experiences, and they can complement a recovery endpoint without measuring the same underlying event.

The posted secondary mortality comparison has an estimated risk difference of 0.026, with a confidence interval from -0.035 to 0.086 and an unadjusted p-value of 0.408. That interval includes zero. The record lists safety outcomes through Day 5, Day 28, and Day 90, but it does not report analyses for those outcomes. Consequently, the secondary information does not form a consistent set of analyzed results from which to draw a broad pattern across all listed outcomes.

Secondary endpoints are often numerous and may be exploratory. When many outcomes are tested, the chance of observing at least one apparently unusual result by chance can increase. Adjustments or a hierarchy of testing can address some multiplicity concerns, but the registry record does not report a multiplicity strategy. Unadjusted secondary p-values, when present, therefore carry less weight than a prespecified primary result interpreted within its analysis plan. They should not be treated as independent confirmation without considering the number of comparisons and their prespecification.

The secondary findings should be understood as contextual rather than decisive. They do not overturn or resolve the uncertainty in the primary estimate, and the absence of posted analyses for some listed endpoints is not evidence that their outcomes were equal between groups. The registry record does not report the detailed secondary analysis plan, the handling of missing outcome data, or whether secondary testing was intended to support formal claims.

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

• Number of Participants Who Died From All Causes
• Number of Participants With a Safety Outcome Through Day 5
• Number of Participants With a Safety Outcome Through Day 28
• Number of Participants With a Safety Outcome Through Day 90

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the stated sustained-recovery definition through Day 90 or did not. The group summaries are counts of participants with the outcome and the number of participants in each group. A comparison of the corresponding proportions can be expressed as a risk difference, risk ratio, or odds ratio. These measures answer related but distinct questions, so their values and interpretations are not interchangeable.

What does the risk difference represent?

A risk difference subtracts one group's observed proportion from the other's. In this comparison, the stated contrast is placebo plus standard of care minus MP0420 plus standard of care. The reported estimate is -0.024. A value of zero would represent equal observed proportions under this contrast; a negative value indicates that the placebo group's observed proportion was lower in the posted data. The estimate is a summary of these trial groups, not a prediction for every participant or a guarantee about future groups.

The risk difference is an absolute measure: it is expressed on the scale of proportions rather than as a ratio. Relative measures can give a different perspective. The risk ratio compares the two proportions by division, while the odds ratio compares the odds of the outcome. Odds are not the same quantity as probabilities. When interpreting any relative estimate, its direction depends on which group is in the numerator and how the contrast is defined. The registry comparison specifies the reference group and the reported ratio estimates.

How should the confidence interval be understood?

A confidence interval describes uncertainty in an estimated group contrast under the statistical method used. It gives a range of values compatible with the data and method at the stated confidence level. It is not a range containing a known proportion of individual participants, and it does not mean that every value inside the interval is equally plausible. The primary risk-difference interval runs from -0.093 to 0.046. Because it spans zero, the posted data do not distinguish the observed contrast from no difference at conventional levels of statistical evidence.

A p-value measures how unusual data at least as incompatible with a null hypothesis would be if that null model and the analysis assumptions held. The primary unadjusted p-value is 0.509. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A p-value should be read alongside the estimated effect and its interval, not as a stand-alone verdict.

What does unadjusted mean in this comparison?

An unadjusted comparison uses the posted group outcome summaries without adjustment for additional participant characteristics or other covariates. Randomization is intended to support a fair comparison of assigned groups, but adjustment can be part of a prespecified analysis strategy. The particular primary analysis model and any adjusted analysis are not reported in the registry record. The reported p-value is explicitly unadjusted, and no separate adjusted estimate is posted in the record.

For a binary outcome, the group counts and denominators determine the observed proportions. Statistical uncertainty then reflects the limited information available from the sample. In general, larger samples can yield more precise estimates when other conditions are similar, while a small number of outcome observations can leave considerable uncertainty. This general principle does not establish the adequacy of the trial's original design; the original sample-size rationale is not reported in the registry record.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. If a model assumes that observations vary only according to its specified probability structure but outcomes are more variable, standard errors can be too small and confidence intervals too narrow. Appropriate modeling can account for extra variability where the outcome and design require it. The primary endpoint is posted as a participant count, and dispersion is not applicable in the same way it is for some continuous or rate outcomes. The registry record does not describe a model-based adjustment for over-dispersion.

More broadly, the endpoint definition and follow-up window determine what the comparison can answer. Sustained recovery combines discharge, survival, and a specified period at home by Day 90. A different recovery definition or follow-up period could produce a different estimand. The record does not report alternative primary definitions or sensitivity analyses, so the posted estimate should be interpreted specifically for the stated definition.

The trial is described as randomized and triple masked, but the allocation procedure, the people covered by masking, and the details of the statistical analysis plan are not reported in the registry record. The official title calls the design adaptive, but the adaptation rules and any effects on the analysis are not reported in the registry record. These absences limit assessment of design and analysis decisions beyond the information in the posted group comparison.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.024, and its confidence interval runs from -0.093 to 0.046. The interval is the main guide to precision: it shows that the estimate is uncertain across a range that includes zero. The point estimate is slightly below zero under the stated placebo-minus-MP0420 contrast, but the interval also extends above zero. Thus the data are compatible with effects in either direction under this measure.

The width of an interval reflects both the amount of information in the data and the variability expected under the analysis. In general, a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the size of the effect. Precision is not the same as importance: a precise estimate can be close to zero, and an imprecise estimate can include effects that would matter to decision-makers. Judging importance requires context beyond the statistical estimate, and no clinical importance threshold is reported in the registry record.

The risk-ratio interval, 0.891 to 1.059, includes 1, its no-association value. The odds-ratio interval, 0.545 to 1.351, also includes 1. These intervals reinforce that the relative-effect summaries do not identify a clear group separation. Since ratio and difference measures use different scales, their interval endpoints should not be compared as if they represented the same quantity.

The unadjusted p-value of 0.509 is consistent with the interval including the null value. Neither statistic demonstrates equivalence or rules out potentially meaningful differences. A formal equivalence or non-inferiority conclusion would require appropriate prespecified margins and methods; those are not reported in the registry record. The most defensible reading is that the posted estimate is uncertain, with the confidence interval conveying a broad range of effects compatible with the data and method.

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 illustrations translate the observed effect into hypothetical planning quantities; they are not the original trial's design justification. For this binary outcome, the figures are participants per arm, not total events. The listed 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 trial design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a future study to have an 80% chance of detecting the assumed effect under the listed planning assumptions, if that effect and those assumptions were correct. The 90% power column gives the corresponding planning quantity for a 90% chance. These are design targets, not probabilities that the current trial's result is correct. The illustrations are not observed power.

For 100% of the observed effect, the illustration gives 4,356 participants per arm for 80% power and 5,831 participants per arm for 90% power. For 75% of the observed effect, it gives 7,653 participants per arm for 80% power and 10,244 participants per arm for 90% power. For 50% of the observed effect, it gives 17,010 participants per arm for 80% power and 22,771 participants per arm for 90% power.

The pattern follows a general planning principle: smaller effects are harder to distinguish from random variation, so more participants are needed to reach the same power target. The figures depend on the observed effect being a reasonable planning basis. Because that estimate is uncertain, these quantities should be treated as illustrations rather than definitive requirements. A planning curve, when read alongside the listed values, represents the same relationship between assumed effect size and the participant count needed under the stated assumptions.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.822; treatment proportion p₁ = 0.798; average p̄ = 0.810.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5547 = 1.0872.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5544 = 0.4666.
4. n = (1.0872 + 0.4666)² / (-0.0235)² = 4,355.9, rounded up to 4,356 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 <- 0.821862348178138                          # control proportion
p1 <- 0.798319327731092                          # 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(5780463)
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 = 4,356 (80% power), 5,831 (90% power)
 75% of observed effect: n per arm = 7,653 (80% power), 10,244 (90% power)
 50% of observed effect: n per arm = 17,010 (80% power), 22,771 (90% power)
power.prop.test: 4355.9 
Simulated power at n = 4,356 per arm: 0.798 (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

Multiplicity arises when several outcomes, time points, comparisons, or subgroup analyses are examined. Even when no real effect exists, repeated testing can increase the chance of at least one apparently notable result. Common approaches include adjusting significance thresholds, controlling an error rate, or specifying a hierarchical testing order in advance. The registry record lists multiple outcomes, but the multiplicity strategy and any prespecified hierarchy are not reported in the registry record. The posted unadjusted comparisons should therefore be interpreted without assuming control of the overall false-positive risk across outcomes.

Missing data can also affect interpretation, especially when an endpoint depends on follow-up status over time. For sustained recovery, participants must be classified according to discharge, being alive, and being at home for the required interval before Day 90. The record does not describe how missing or indeterminate endpoint status was handled, whether imputation was used, or whether sensitivity analyses assessed alternative assumptions. Those details are not reported in the registry record.

The primary analysis population is not specified in the endpoint record. Although the study is randomized, the registry record does not state whether the analysis followed an intention-to-treat, modified intention-to-treat, per-protocol, or other population definition. It also does not report the number of participants included in each analysis population or how participants with protocol deviations were treated. These omissions make it difficult to assess whether the analyzed groups corresponded to all randomized participants or a subset defined by additional criteria.

The official title calls the trial adaptive, but details of any interim looks, adaptation rules, stopping criteria, or adjustments to inference are not reported in the registry record. The record also does not provide the original statistical analysis plan or the full specifications of the primary statistical method. These points matter because interim monitoring and adaptive decisions can influence how final estimates and significance tests should be interpreted.

These gaps do not invalidate the posted counts or comparison, but they limit independent evaluation of how outcomes were selected, analyzed, and interpreted. The primary estimate and its interval remain useful summaries of the posted data; conclusions beyond that summary should acknowledge that the analysis population, missing-data procedures, and multiplicity handling are not reported in the registry record.

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: pneumothorax (0.8%), deep vein thrombosis (0.8%), anaemia (0.4%), atrial fibrillation (0.4%), gastrointestinal hemorrhage (0.4%).

The registry record lists counts of participants with serious adverse events and other adverse events in each group. For serious adverse events, the counts are 14 among 247 participants in the MP0420-plus-standard-of-care group and 18 among 238 participants in the placebo-plus-standard-of-care group. For other adverse events, the counts are 65 and 79, respectively, with the same group denominators. These are participant counts, not counts of every event episode.

The record also lists deaths through Day 90 as a secondary outcome, with counts of 30 in the MP0420 group and 35 in the placebo group. Serious adverse event terms appearing among the most frequently listed include pneumothorax and deep vein thrombosis at 0.8% each, and anaemia, atrial fibrillation, gastrointestinal hemorrhage, and abdominal wall hematoma at 0.4% each. These term percentages are reported as listed in the registry record.

Counts alone do not establish whether an event was caused by a study treatment. They also do not indicate event severity beyond the serious-event classification, duration, recurrence, or the relationship between an event and an individual participant's clinical course. The registry record does not report comparative statistical analyses for these safety summaries. They should be read descriptively, with attention to group sizes and the limits of the information recorded.

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

The primary result is a comparison of the proportion of participants meeting a defined sustained-recovery outcome through Day 90. The observed risk difference is -0.024 under the placebo-minus-MP0420 contrast, and its confidence interval includes zero. The unadjusted p-value is 0.509. Taken together, these statistics do not provide strong evidence of a difference in the posted primary comparison, while leaving uncertainty about the direction and size of any difference.

That interpretation is narrower than saying that the treatments are equivalent. Equivalence requires a defined margin and an analysis designed to show that any difference lies within that margin. A non-inferiority conclusion likewise requires a prespecified margin and corresponding methods. Such margins and analyses are not reported in the registry record. The result should not be recast as proof that there is no difference.

The comparison also does not show that MP0420 alone was compared with no treatment. Both groups received standard of care, with remdesivir provided unless contraindicated. The randomized contrast concerns MP0420 versus placebo on top of that background care. The results do not isolate the contribution of remdesivir or other standard-care components.

The endpoint has a specific meaning: discharge from the index hospitalization followed by being alive and at home for 14 consecutive days before Day 90. It is not a measure of every dimension of recovery, nor does it describe outcomes beyond the stated follow-up window. Different definitions, follow-up periods, or patient groups could yield different estimates; those alternatives are not evaluated in the posted primary result.

Finally, group summaries describe average outcomes in the trial, not an individual's likely course. The record does not report subgroup results or enough detail to establish whether the estimate varies across participant characteristics. The findings should be treated as a statistical description of this randomized study's posted outcomes, with the confidence interval and registry limitations kept in view—not as individualized guidance or a guarantee of benefit or harm.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through both its effect estimate and its uncertainty. The arm-level counts describe what happened in the enrolled groups, while the risk difference expresses the observed contrast on an absolute scale. The confidence interval shows that the estimate is not precise enough to identify a clear direction of effect. Looking only at the point estimate or only at the p-value would discard important information.

It also demonstrates the importance of defining the endpoint carefully. Sustained recovery is not simply discharge: it requires a subsequent period alive and at home before Day 90. Statistical interpretation depends on that operational definition. A statement about this endpoint cannot automatically be extended to other definitions of recovery, outcomes beyond Day 90, or unreported subgroups.

The distinction between the randomized contrast and background care matters as well. Both groups received standard of care, and remdesivir was provided unless contraindicated. The estimate therefore concerns the addition of MP0420 compared with placebo within that care setting. Correctly identifying the comparator prevents an overbroad interpretation of what the trial tested.

Finally, the registry record leaves important analysis details unreported, including the original sample-size justification, analysis population, missing-data procedures, and multiplicity strategy. These absences limit assessment of the full statistical plan, even though the posted estimate and interval remain interpretable as summaries. The planning illustrations also show how sample-size requirements depend on assumptions about effect size and power; they are not substitutes for the original design rationale or a measure of the current trial's observed power.

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.

Several limitations are specific to the information recorded for this trial. The primary endpoint is a composite sequence involving discharge, survival, and being at home for 14 consecutive days before Day 90. The registry record does not report the separate contribution of each component, so the overall count cannot show which part of the definition most often determined whether a participant met the endpoint.

The trial is labeled adaptive, but the registry record does not describe the adaptations, interim analyses, or any implications for the final statistical inference. Triple masking is reported, but the roles covered by masking and the allocation procedures are not described. The original sample-size justification and statistical analysis plan are also not reported, limiting review of how the planned analysis aligns with the posted result.

The record does not specify the primary analysis population or how missing and indeterminate outcome data were handled. It also does not report sensitivity analyses, subgroup estimates, or adjusted analyses. These omissions mean that the robustness of the estimate to alternative analysis choices cannot be assessed from the posted results alone.

For secondary outcomes, analyses are not reported in the registry record for the listed safety outcomes. The record lists descriptive adverse-event counts but does not provide comparative statistical analyses for those summaries. A lack of posted analysis is not evidence that the groups had the same outcome. More generally, adverse-event counts do not establish treatment causality.

The primary confidence interval includes zero and spans effects in either direction. This imprecision limits how specifically the result can be interpreted. In addition, the primary comparison concerns participants hospitalized with COVID-19 under the recorded standard-of-care context; the registry information does not establish how the estimate applies to settings or populations not represented in the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: MP0420 for Inpatients With COVID-19 (An ACTIV-3/TICO Treatment Trial) — NCT05780463.
• Registry record last updated 2024-02-05; status last verified 2024-02.
• Results first posted 2024-02-05.
• 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

NCT05780463 is a completed Phase 3 randomized, triple-masked, parallel-group trial of MP0420 plus standard of care compared with placebo plus standard of care in hospitalized patients with COVID-19. The registry record lists enrollment of 485 and identifies the National Institute of Allergy and Infectious Diseases (NIAID) as sponsor.

The primary outcome is sustained recovery through Day 90, defined as discharge from the index hospitalization followed by being alive and at home for 14 consecutive days before Day 90. The posted counts are 203.0 of 247.0 participants in the MP0420 group and 190.0 of 238.0 in the placebo group. The risk difference is -0.024, with a confidence interval from -0.093 to 0.046 and an unadjusted p-value of 0.509.

The interval includes zero, leaving uncertainty about the direction and size of the group difference. The record lists secondary mortality and safety outcomes, but analyses are not reported for the listed safety outcomes. Details of the original sample-size rationale, analysis population, missing-data handling, multiplicity strategy, and adaptive procedures are not reported in the registry record.