LY3819253 (LY-CoV555) 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 LY3819253 (LY-CoV555) for Inpatients With COVID-19 (An ACTIV-3/TICO Treatment Trial) (NCT05780268), a randomized phase 3 study. The primary outcome is Number of Participants With Sustained Recovery.

2. Clinical Question

This is a comparison of assigned treatment groups among hospitalized people, with recovery defined by both discharge and a sustained period alive at home. It does not ask only whether a participant was discharged, nor does it measure symptom change in isolation. The endpoint's definition joins a hospital event with subsequent status over time, so it represents a more sustained outcome than discharge alone.

The record identifies the trial as part of ACTIV-3/TICO Treatment Trial H1. Its stated focus was safety and effectiveness of LY3819253 in hospitalized patients with COVID-19. The registry record does not report further details of the eligibility criteria, such as the clinical characteristics required at enrollment, or the specific care setting beyond hospitalization. Interpretation should therefore remain anchored to the recorded population and treatment contrast rather than extending the result to people or settings not described.

3. Trial Design

This was a phase 3, randomized, triple-blind, parallel-group trial. The registry record reports an enrollment of 314 participants and a completed status. The listed start date is 2020-08-05, and the primary completion date is 2021-02-01. The sponsor is the National Institute of Allergy and Infectious Diseases (NIAID). The official title describes a multicenter, adaptive, randomized, blinded controlled trial; the record does not report the operational details of any adaptation or the number and locations of participating centers.

The two groups were LY3819253 plus standard of care and placebo plus standard of care. The posted primary outcome counts are 144 of 163 in the LY3819253 group and 136 of 151 in the placebo group. These are the group counts associated with the primary sustained-recovery outcome. Remdesivir was specified as standard care for participants unless contraindicated for an individual patient. Therefore, the randomized contrast concerns the addition of LY3819253 rather than a comparison of remdesivir with no remdesivir.

Random assignment is intended to make the treatment groups comparable, on average, with respect to factors that could affect the outcome. Blinding is intended to limit the influence of treatment knowledge on care, outcome assessment, or participant reporting. The record labels masking as triple, but does not identify the specific groups of people masked or describe how masking was maintained. Allocation concealment procedures and the method used to generate the random sequence are not reported in the registry record.

The registry record labels the design adaptive, but the particular adaptations, decision rules, timing, and consequences for enrollment or analysis are not reported in the registry record. The original sample-size target and its justification are also not reported. The posted planning illustrations based on observed effects should not be read as documentation of the trial's original design assumptions.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

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

The primary endpoint is the number of participants with sustained recovery through Day 90. A participant counted as recovered had to be discharged from the index hospitalization and then remain alive and at home for 14 consecutive days before Day 90. The outcome is binary at the participant level: each participant either met that definition or did not. The posted counts are 144 of 163 for LY3819253 plus standard care and 136 of 151 for placebo plus standard care.

This definition combines discharge with a period of subsequent stability at home. That makes the outcome more demanding than discharge alone: a discharge without the required time alive and at home would not meet the stated definition. It also gives the endpoint a concrete interpretation relevant to hospital recovery, while setting a defined observation horizon through Day 90.

In general, a prespecified primary endpoint gives a trial a principal outcome around which its main comparison is organized. A clear definition helps readers understand what event was counted and which participants meet the criterion. Here, the endpoint does not directly describe the length of hospitalization, quality of life, symptoms, or each component separately. The registry record does not report a separate analysis of the discharge component or the subsequent period at home, so the posted primary result should be interpreted as the combined sustained-recovery outcome.

7. Results Posted in the Registry

• Placebo Plus SOC: 90.1% (136/151) versus 88.3% (144/163) on control; risk difference 1.7 percentage points (95% CI -5.1 to 8.6), risk ratio 1.02 (0.94–1.10); unadjusted two-proportion z-test p = 0.624.

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: 7.3% (11/151) versus 8.0% (13/163) on control; risk difference -0.7 percentage points (95% CI -6.6 to 5.2), risk ratio 0.91 (0.42–1.98); unadjusted two-proportion z-test p = 0.818.
• 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 secondary outcomes broaden the questions beyond sustained recovery. They include all-cause death through Day 90 and safety outcomes through Day 5, Day 28, and Day 90. These outcomes can add context about survival and safety over follow-up, but they address different events and time windows from the primary endpoint. Their results should not be treated as interchangeable with the sustained-recovery comparison.

The registry posts a comparison for the all-cause death outcome, while the reported-analyses list is empty and the safety outcomes are listed without a corresponding set of outcome comparisons. The available secondary information is therefore limited. It does not form a coordinated set of estimates that independently confirms or overturns the primary result. In particular, an outcome being named as secondary does not mean that a numerical treatment comparison or complete analysis details are available in the record.

In general, secondary outcomes can be useful for describing additional effects and for identifying patterns worth further study. Their evidential weight depends on how they were prespecified, how many outcomes were tested, whether analyses were adjusted for multiple comparisons, and how complete the reporting is. The multiplicity plan and detailed analysis methods are not reported in the registry record. Unadjusted secondary findings, when many outcomes are considered, carry less confirmatory weight because the chance of at least one apparently notable result can increase with repeated testing.

The secondary outcomes should therefore be read as supplementary information, not as a substitute for the primary endpoint or as a set of independent definitive conclusions. Their different definitions, assessment windows, and reporting completeness matter when considering whether they are consistent with the primary result. The record does not provide enough detail to determine a formal hierarchy or to make a multiplicity-adjusted interpretation across all outcomes.

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

In general, a binary endpoint records whether each participant meets a defined condition. For this trial, the condition is sustained recovery by the stated definition. The registry posts the number meeting the endpoint and the number in each assigned group. A group proportion expresses the observed count relative to the number in that group; the posted proportions are 0.883 for LY3819253 plus standard care and 0.901 for placebo plus standard care.

What does a risk difference express?

In general, a risk difference subtracts one group's event proportion from the other's. It remains on the absolute scale of the outcome, unlike a risk ratio or odds ratio, which express a relative comparison. The posted risk difference is 0.017 for placebo relative to LY3819253. The confidence interval runs from -0.051 to 0.086. Values below zero and above zero represent opposite directions of the group contrast, while zero represents no difference on this scale. The direction should always be read with the group ordering in mind.

The registry also includes relative measures for the primary comparison: a risk ratio of 1.019 with a confidence interval from 0.944 to 1.101, and an odds ratio of 1.196 with a confidence interval from 0.584 to 2.449. In general, a risk ratio compares probabilities, whereas an odds ratio compares odds. These measures use different scales and should not be read as though they were risk differences. Their intervals include the corresponding no-association value of one, just as the risk-difference interval includes zero. No adjusted analysis is reported in the registry record.

What does the confidence interval add?

In general, a confidence interval describes the range of effect estimates reasonably compatible with the observed data under the method's assumptions. It captures uncertainty in estimation, not the range of outcomes that individual participants experienced. A wider interval indicates less precision than a narrower interval on the same scale. For the primary risk difference, the interval extends across zero and permits effects in either direction, so the estimate does not pin down the direction or magnitude very precisely.

The unadjusted p-value for the primary comparison is 0.624. In general, a p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions were true. It is not the probability that the null model is true, and it does not measure the size or importance of an effect. The registry labels this value unadjusted. The method used to calculate the displayed comparison and p-value is not reported in the registry record.

Why can binary outcomes be over-dispersed?

In general, over-dispersion means that observed variability is greater than a model assumes. For binary outcomes, this can arise when participants differ in their underlying event probabilities or when outcomes are correlated within groups such as centers. If a model assumes more independence or uniformity than the data support, its standard errors can be too small and its confidence intervals too narrow. That concern is general; the registry record does not report an over-dispersion assessment or a model designed to address it. The posted summary does not establish whether such issues were evaluated in the trial analysis.

The registry gives group counts and a comparison, but does not report the analysis population definition, missing-data handling, or whether any participants were excluded from the primary analysis after randomization. It also does not report a covariate-adjustment set or sensitivity analyses. Such details matter because analysis choices can affect both the estimate and the uncertainty, particularly if outcome status is missing or if analysis populations differ from all randomized participants. Without those details, interpretation should be restricted to the results as posted.

The outcome is described as the number of participants with sustained recovery through Day 90. Although this is a time-bounded event definition, the posted analysis is a binary count comparison, not a time-to-event analysis. It does not provide information on how quickly recovery occurred among participants who recovered. The registry record does not report a separate estimate of time to recovery in the posted results.

The trial is identified as adaptive, but its actual adaptation rules and any impact on statistical testing are not reported in the registry record. In general, adaptive designs can use accumulating information to guide prespecified changes, but valid inference depends on the specific rules and methods used. No particular adaptation, interim look, stopping boundary, or adjustment for repeated testing can be inferred from the design label alone.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.017, with a 95% confidence interval from -0.051 to 0.086. Because this interval includes zero, the observed data are compatible with no risk difference as well as with differences in either direction. The estimate itself is close to zero, but the interval indicates uncertainty around that estimate; it is not narrow enough to support a precise claim that the groups have the same sustained-recovery outcome.

In general, a confidence interval is a measure of estimation precision under the analysis method. It is not a guarantee that the true effect lies within the particular interval, nor does it describe how much individual outcomes vary. A confidence interval can also contain values that differ in practical importance. Judging practical importance requires a context for what sizes of difference would matter; such a threshold is not reported in the registry record.

The relative-scale intervals likewise include their no-association value: the risk ratio is 1.019 with an interval from 0.944 to 1.101, and the odds ratio is 1.196 with an interval from 0.584 to 2.449. The odds-ratio interval is especially broad on its scale. These measures do not remove the uncertainty apparent on the absolute scale. The registry does not report a prespecified precision target or a noninferiority or equivalence margin, so the results cannot be interpreted as a formal equivalence finding.

The group sizes were 163 and 151 for the primary outcome. Precision depends on the amount of information in the data and on the outcome and analysis assumptions; a point estimate alone does not convey it. The confidence interval is therefore central to interpretation: the posted data do not identify a clear difference, but they also do not rule out all potentially relevant differences.

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 illustrations are based on the observed effect, not on the trial's original design. For the participant outcomes displayed, the figures are participants per arm, not total participants across both arms and not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use an effect to detect equal to the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The columns for 80% and 90% power describe planning targets. In general, power is the chance that a study design would identify an effect at a chosen significance level if that effect were the true effect and the planning assumptions held. A design planned for 80% power has a lower detection probability under those assumptions than one planned for 90% power, and the higher target generally requires more participants. These are planning calculations, not observed power.

For the primary sustained-recovery outcome, planning for 100% of the observed effect gives 5,093 participants per arm for 80% power and 6,818 participants per arm for 90% power. Planning for 75% of the observed effect gives 9,213 and 12,334 participants per arm, respectively. Planning for 50% gives 21,086 and 28,227 participants per arm, respectively. The mortality planning figures also refer to participants per arm because that is a participant outcome, rather than total events.

The pattern illustrates a general feature of planning: smaller effects require more participants to distinguish them from random variation at the same power target and significance level. These illustrations should not be used to infer the trial's original intended effect, planned enrollment, or success probability. They use the observed effect as an input and do not convert the completed trial's result into an estimate of its power.

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 = 0.883; treatment proportion p₁ = 0.901; average p̄ = 0.892.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4389 = 0.8601.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4387 = 0.3692.
4. n = (0.8601 + 0.3692)² / (0.0172)² = 5,092.7, rounded up to 5,093 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 <- 0.883435582822086                          # control proportion
p1 <- 0.900662251655629                          # 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(5780268)
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 = 5,093 (80% power), 6,818 (90% power)
 75% of observed effect: n per arm = 9,213 (80% power), 12,334 (90% power)
 50% of observed effect: n per arm = 21,086 (80% power), 28,227 (90% power)
power.prop.test: 5092.7 
Simulated power at n = 5,093 per arm: 0.806 (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, comparisons, time points, or interim analyses are examined. In general, repeated testing can increase the chance of obtaining at least one result that appears statistically notable by chance, even when there is no true effect. A prespecified testing hierarchy or adjustment procedure can control that issue, but it must be interpreted in light of the actual plan and the analyses performed.

This trial has a primary endpoint and several secondary outcomes, including safety assessments at different follow-up times. The registry record does not report a multiplicity adjustment, a testing hierarchy, or whether the secondary outcomes were intended to support confirmatory claims. It also does not report the detailed protocol or statistical analysis plan. The posted unadjusted p-values should therefore not be treated as if they had been adjusted for all outcomes or repeated looks. The trial's adaptive label alone does not establish whether interim analyses occurred or how any repeated testing was handled.

Missing outcome data can also affect interpretation. The registry record does not report the number of participants with missing Day 90 status, how missingness was handled, whether participants were analyzed according to randomized assignment, or whether any sensitivity analyses were conducted. It is therefore not possible to establish from this record whether every randomized participant was included in the primary analysis or how incomplete follow-up may have influenced the posted counts.

The record does not report the definitions of the analysis populations, such as intention-to-treat or per-protocol populations, nor does it provide a participant flow account showing exclusions after randomization. It also does not report whether outcome assessment was centralized, how sustained recovery was verified, or how ambiguous cases were classified. These omissions do not demonstrate that appropriate procedures were absent; they mean that the registry record does not provide those details for independent interpretation.

In general, conclusions are strongest when the primary outcome, analysis population, missing-data rules, and multiplicity approach are prespecified and transparently reported. Here, the primary outcome and its endpoint definition are stated, but several analysis safeguards and implementation details are not reported in the registry record. Readers should keep that reporting limitation in mind when interpreting both the primary comparison and the less fully documented secondary outcomes.

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: chronic obstructive pulonary disease (1.3%), atrial fibrillation (0.7%), coronary artery stenosis (0.7%), diarrhoea (0.7%), intestinal ischaemia (0.7%).

The registry reports serious adverse events in 9 of 163 participants assigned LY3819253 plus standard care and 12 of 151 assigned placebo plus standard care. Other adverse events are reported in 41 of 163 and 27 of 151 participants, respectively. Deaths are listed as 13 and 11 participants in the two groups. These are counts of participants reported in the registry's safety results; they are not, by themselves, estimates of causal effects or adjusted comparisons.

The listed serious-event terms include Chronic obstructive pulonary disease at 1.3%, and Atrial fibrillation, Coronary artery stenosis, Diarrhoea, Intestinal ischaemia, and Vomiting at 0.7% each. The registry record does not give the detailed event-level context needed to interpret these terms, such as onset, duration, attribution, or overlap between participants and events. The record also does not provide comparative statistical analyses for these safety counts in the reported analyses.

In general, safety counts need to be interpreted with attention to follow-up duration, event definitions, exposure, and the distinction between events and participants affected. The counts describe what was recorded in these trial groups; they do not alone establish that treatment caused or prevented an event. The registry's listed safety time points include follow-up through Day 5, Day 28, and Day 90, but detailed analyses for each timeframe are not posted.

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

The primary result describes sustained recovery through Day 90 among participants assigned to the two trial groups. The observed proportions were 0.883 with LY3819253 plus standard care and 0.901 with placebo plus standard care. The estimated risk difference for placebo relative to LY3819253 was 0.017, and the confidence interval crossed zero. The posted comparison therefore does not provide clear statistical evidence of a difference in this endpoint between the groups.

That finding is not proof that the treatments are equivalent. A formal equivalence conclusion would require a prespecified margin and an analysis designed to assess whether the full confidence interval lies within that margin; neither is reported in the registry record. Nor does a nonsignificant comparison establish that no effect exists. The confidence interval retains uncertainty about the size and direction of the difference.

The result also does not establish that LY3819253 is beneficial or harmful, or that placebo is preferable. It reports a randomized group comparison in the context of standard care, including remdesivir unless contraindicated. Individual participants could have different outcomes, and the group estimate does not predict any particular person's recovery. No medical decision should be inferred from this registry result alone.

The record's scope is hospitalized people with COVID-19 enrolled in this trial. It does not establish effects in non-hospitalized people, in other populations, or under care conditions different from the trial's described standard-care context. Eligibility detail and participant characteristics are not reported in the registry record, which further limits assessment of how broadly the findings apply.

Finally, the posted outcome and analysis information does not include all details needed for a complete methodological audit. Missing-data methods, analysis-population definitions, multiplicity handling, and the specific adaptive design procedures are not reported. The most restrained interpretation is that the primary estimate is near zero on the risk-difference scale, but remains uncertain, and that the registry record does not establish a definitive treatment difference or equivalence.

17. Why This Trial Matters Statistically

This trial illustrates why an estimate and its uncertainty need to be read together. The primary point estimate is close to zero, but the confidence interval spans zero and includes effects in both directions. A conclusion based only on which group has the numerically larger observed proportion would overstate what the data establish. Likewise, a p-value alone does not describe the magnitude or precision of the comparison.

The endpoint also shows how definition shapes interpretation. Sustained recovery requires discharge followed by being alive and at home for 14 consecutive days before Day 90. That is more specific than a simple discharge outcome and combines multiple aspects of recovery into a single participant-level classification. Readers need the endpoint definition to understand what the event counts represent and what they do not measure.

The trial's randomized, blinded design is important to the context of the comparison, but design labels do not substitute for reporting the methods. The registry identifies a phase 3 adaptive trial and triple masking, while operational details of the adaptations, randomization procedures, and analysis plan are not reported. This distinction is useful more broadly: a design description indicates the intended structure, but the inferential strength also depends on the implementation and transparent analysis.

The sample-size illustrations further demonstrate that planning requirements depend on the effect size one aims to detect. Smaller effects require more participants under the stated planning assumptions, and the observed-effect illustrations are not evidence of the original target or of observed power. Finally, the limited secondary-analysis reporting makes clear why a set of outcomes should not automatically be treated as multiple independent confirmations. Statistical interpretation depends on prespecification, precision, multiplicity, and completeness of reporting.

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 specific to this registry record affect interpretation. The record does not report detailed eligibility criteria or participant characteristics, so the enrolled population cannot be described beyond being hospitalized with COVID-19. The total enrollment is reported, but a participant flow account and the primary analysis population are not. It is not reported how many participants had missing Day 90 outcome status or how any such missingness was handled.

The registry identifies the study as adaptive but does not report the adaptation rules, interim analyses, decision boundaries, or any resulting changes to the design. The original sample-size target and its justification are also not reported. The posted planning illustrations use the observed effect and should not be mistaken for the trial's original planning basis.

Statistical detail is limited: the record does not report a full model specification, covariate adjustment, analysis method for the primary comparison, sensitivity analyses, multiplicity procedures, or a hierarchy for secondary testing. The reported analyses list is empty, and the secondary safety outcomes do not have posted comparison analyses in that list. These omissions constrain independent assessment of robustness and the relative evidential weight of secondary findings.

The primary endpoint combines discharge and a subsequent period alive at home. The record does not post separate component analyses or a time-to-recovery analysis, so it is not possible to distinguish which part of the definition accounts for the observed group counts. The safety counts are also not accompanied by detailed event-level context or comparative analyses. These are limitations of the information reported in the registry record; they do not establish that additional analyses or documentation were absent elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: LY3819253 (LY-CoV555) for Inpatients With COVID-19 (An ACTIV-3/TICO Treatment Trial) — NCT05780268.
• Registry record last updated 2023-12-27; status last verified 2023-12.
• Results first posted 2023-10-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed phase 3 randomized, triple-blind, parallel-group trial of LY3819253 plus standard of care versus placebo plus standard of care in hospitalized people with COVID-19. Enrollment was 314. The primary endpoint was 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 primary counts were 144 of 163 participants in the LY3819253 group and 136 of 151 in the placebo group. The reported risk difference for placebo relative to LY3819253 was 0.017, with a 95% confidence interval from -0.051 to 0.086 and an unadjusted p-value of 0.624. The estimate is compatible with no difference, but the interval does not establish equivalence.

The record also lists death and safety outcomes. Important details about missing data, analysis populations, multiplicity, and the adaptive procedures are not reported in the registry record, limiting the methodological detail available for interpretation.