A Study of Brexanolone for Acute Respiratory Distress Syndrome (ARDS) Due to Coronavirus Disease 2019 (COVID-19): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Brexanolone for Acute Respiratory Distress Syndrome (ARDS) Due to Coronavirus Disease 2019 (COVID-19) (NCT04537806), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Are Alive and Free of Respiratory Failure at Day 28.

2. Clinical Question

The comparison is between the observed Day 28 outcome in the brexanolone group and the placebo group. It is a binary outcome: each participant with available data is classified according to whether they were alive and free of respiratory failure at the specified time. The reported percentages are 23.1% in each group. The posted comparison therefore has a risk difference of 0.0, with a 95% confidence interval from -0.324 to 0.324 on the risk-difference scale and an unadjusted p-value of 1.0.

This describes the result for the participants included in the posted analysis, not a universal effect estimate for all people with COVID-19 or ARDS. The registry record states that the primary analysis population included randomized participants who initiated study treatment, and that the analyzed number means participants with available data. It does not report further detail about how missing endpoint values were handled or about the reasons participants did not contribute primary-outcome data.

3. Trial Design

This was a randomized, triple-masked, parallel-group Phase 3 study of brexanolone and placebo. The stated purpose was to evaluate the efficacy and safety of brexanolone among participants receiving ventilator support for ARDS due to COVID-19. Mechanical ventilation was standard of care in both groups. The intervention was a continuous intravenous infusion of brexanolone, while the comparator received matching placebo.

The registry lists enrollment as 29 and the status as terminated. The start date is 2020-12-18, and the primary completion date is 2021-07-01. The reason for termination is not reported in the registry record. The planned enrollment target, the number of sites, and the allocation ratio are not reported in the registry record. Although the groups were randomized, details about the randomization sequence and concealment are not reported in the registry record.

For the primary endpoint, 13 participants were analyzed in each group. The endpoint analysis population is described as all randomized participants who initiated study treatment, with the analyzed number representing those with available data. The secondary death outcome uses 14 participants in each group. These different analysis denominators are reported as recorded; further explanation for the distinction is not reported in the registry record.

The study included one posted primary analysis. The registry lists three outcome measures and two secondary outcomes. The named secondary outcomes include participants with at least one treatment-emergent adverse event and participants who died through Day 28. A result for the treatment-emergent adverse-event outcome is not reported in the registry record, although separate safety counts are listed. The study's full statistical analysis plan, the planned handling of multiple outcomes, and details of any interim analyses are not reported in the registry record.

Randomization is intended to make the groups comparable on average, while masking is intended to limit influences on care, assessment, or reporting. These are general design aims, not proof that all potential sources of bias were eliminated in this particular study. With a small analyzed population and a terminated study, the reported group estimates are imprecise, and the registry record does not give enough detail to assess all aspects of conduct or analysis.

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: A total of 33 participants were screened of which 29 were randomized and 28 were dosed. This study consisted of up to a 2-day screening period, a 60-hour treatment period plus an additional follow-up of up to 23 days.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all randomized participants who initiated IP (brexanolone or placebo). Here, "Overall number of participants analyzed" signifies the number of participants with available data for analysis.

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: FAS included all randomized participants who initiated IP (brexanolone or placebo).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Are Alive and Free of Respiratory Failure at Day 28, measured over Day 28.

The primary endpoint is the percentage of participants who were alive and free of respiratory failure at Day 28. It combines survival and respiratory status into one binary outcome. A participant must meet both parts of the description: being alive and not meeting the registry's definition of respiratory failure at the assessment time. The definition uses respiratory-support resources, including endotracheal intubation and mechanical ventilation, high-flow nasal cannula oxygen at the stated flow and oxygen concentration thresholds, noninvasive positive pressure ventilation, and extracorporeal membrane oxygenation.

In general, a combined endpoint can summarize more than one clinically important dimension in a single measure. It can also make interpretation dependent on each component and on how the components are defined. Here, the endpoint reflects both survival and the need for specified respiratory support; it does not separately show the result for each component. The registry record does not report component-specific primary results.

The outcome is measured at Day 28, so it captures status at a specified time rather than the timing or duration of respiratory failure. It should not be read as a complete account of recovery or later outcomes. The posted percentages are 23.1% in each group, with 3 participants meeting the endpoint in each analyzed group. Those figures describe the endpoint as recorded and do not, on their own, establish why participants did or did not meet it.

7. Results Posted in the Registry

• Brexanolone: 23.1% (3/13) versus 23.1% (3/13) on control; risk difference 0.0 percentage points (95% CI -32.4 to 32.4), risk ratio 1.00 (0.25–4.07); unadjusted two-proportion z-test p = 1.000.

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 Through Day 28

• 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:
  • Brexanolone: 57.1% (8/14) versus 42.9% (6/14) on control; risk difference 14.3 percentage points (95% CI -22.4 to 50.9), risk ratio 1.33 (0.63–2.84); unadjusted two-proportion z-test p = 0.450.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Brexanolone and the control. The interval gives the range of effects that remain compatible with the data.

The registry names two secondary outcomes: participants with at least one treatment-emergent adverse event and participants who died through Day 28. The death outcome has a posted comparison. The treatment-emergent adverse-event outcome is not reported as a result in the registry record. Separate serious and other adverse-event counts are present, but they should not be treated as a complete substitute for the named treatment-emergent adverse-event endpoint because the definitions and relationship between these listings are not fully described.

The secondary death comparison is statistically uncertain. Its recalculated risk difference is 0.143, and the 95% confidence interval ranges from -0.224 to 0.509. The unadjusted p-value is 0.45. These figures do not establish a clear difference between groups, and the interval allows for effects in either direction. The registry record does not report a sponsor analysis for this secondary comparison.

This secondary outcome is related to the primary endpoint because survival is one component of being alive and free of respiratory failure. It is not the same outcome: the primary endpoint also requires freedom from the specified respiratory-support criteria, while the secondary endpoint counts death through Day 28. The two results therefore answer different questions and cannot be treated as interchangeable evidence.

Secondary results generally carry less weight than a prespecified primary result, particularly when several outcomes are examined. In general, testing multiple outcomes increases the chance of observing a seemingly notable result by chance unless the analysis plan accounts for multiplicity. The registry record does not report how multiplicity was handled or whether the secondary outcomes were part of a formal testing hierarchy. The secondary findings should consequently be read as supportive descriptive information, not as independent confirmation of the primary result.

The registry includes planning illustrations based on the observed death effect, but those are not results and do not change the interpretation of the secondary comparison. Nor do they indicate the original study's planned power. The overall secondary evidence remains incomplete because a result for the named treatment-emergent adverse-event outcome is not reported in the registry record.

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

• Number of Participants With at Least One Treatment-Emergent Adverse Event (TEAE)
• Number of Participants Who Died Through Day 28

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it classifies each analyzed participant as either alive and free of respiratory failure at Day 28 or not meeting that combined condition. For a binary outcome, the percentage in each group gives the observed proportion meeting the endpoint. The comparison presented is a risk difference: the proportion in the brexanolone group minus the proportion in the placebo group. A value of 0.0 means the estimated proportions are equal in the posted data. The registry reports the group percentages as 23.1% and 23.1% and the risk difference as 0.0.

What does the confidence interval add?

A confidence interval describes statistical uncertainty in an estimated effect. In repeated use of the same method under its assumptions, intervals constructed at a stated confidence level have a specified long-run coverage property. For an individual study, it is best read as a range of effect values reasonably compatible with the data and method, rather than as a guarantee about the true effect. The posted primary interval is at the 95% level and runs from -0.324 to 0.324 on the risk-difference scale. It includes zero, as well as values on either side of zero. It is therefore consistent with no observed difference while also leaving substantial uncertainty about the size and direction of a possible difference.

How should the p-value be read?

The registry's reported primary analysis uses a Chi-squared method under Proc Genmod. The reported estimate is 0.0, its confidence limits are -31.8 to 31.8, and the reported p-value is 1.000. The posted unadjusted calculation also gives a p-value of 1.0. In general, a p-value is calculated under a null hypothesis and statistical model; it indicates how unusual data at least as incompatible with that null would be if the null and model assumptions held. It is not a measure of clinical importance, a probability that the null hypothesis is true, or a test of equivalence. No equivalence margin is reported in the registry record.

Why can counts and percentages be uncertain?

With a binary outcome, each participant contributes one outcome classification. When the number analyzed is small, changing the classification of a participant can have a comparatively large effect on the estimated percentage. Confidence intervals represent this sampling uncertainty. General methods for binary outcomes may use approximations or model-based assumptions; the record names the sponsor's analysis method, but does not report enough detail to reconstruct every modeling choice or diagnostic assessment.

Over-dispersion is a general concern when observed binary outcomes vary more than a model's assumptions allow. If present, it can make standard errors too small and intervals too narrow unless the model accounts for it. The registry record does not report an over-dispersion assessment, so no conclusion about whether it occurred in this study is warranted. This general issue is distinct from the specific uncertainty reflected in the posted interval.

What does the secondary planning illustration mean?

The registry includes a planning illustration for the secondary death outcome. It is computed from the observed effect and assumes a two-sided significance level of 0.05, equal allocation, and a normal approximation. The listed scenarios are planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For 80% power, the corresponding participants per arm are 192, 341, and 765; for 90% power, they are 256, 455, and 1,023.

These are planning illustrations, not the original trial's design calculations and not observed power. They indicate how planning requirements depend on the effect size chosen for a future design under the stated assumptions. The registry record does not report the trial's own sample-size justification, intended effect size, or power target. The illustration concerns death, not the primary endpoint, and should not be used as evidence that the primary analysis had a particular power.

What can the re-calculation establish?

A recalculated comparison based on posted summary statistics is a simple unadjusted analysis. It can provide a transparent check on the contrast and uncertainty implied by the displayed counts and percentages. It cannot reproduce unreported participant-level analyses, adjust for unreported covariates, establish the reasons for missing data, or supersede a sponsor analysis when the two disagree. In this case, the registry indicates no discrepancy between the reported and recalculated primary results. The sponsor's own analysis remains the principal reported analysis.

The primary endpoint population is described as randomized participants who initiated study treatment, with available data defining the analyzed number. This is not enough detail to determine how missing outcomes were handled or whether sensitivity analyses were performed. The record lists one primary analysis but does not provide a full analysis plan, model specification, or interim-analysis information. These omissions limit independent assessment of the statistical procedures beyond the posted result.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of 0.0, based on 23.1% meeting the endpoint in each group. Its 95% confidence interval extends from -0.324 to 0.324. The interval includes zero and is wide enough to encompass differences in either direction. The result therefore has limited precision: the point estimate is centered on no observed difference, but the data do not tightly pin down the size or direction of a possible underlying difference.

Precision is not the same as statistical significance. The p-value of 1.0 reflects the primary test under its assumptions; the confidence interval communicates uncertainty in the magnitude of the risk difference. Neither measure establishes equivalence. To claim equivalence would require an appropriate design and a prespecified margin, neither of which is reported in the registry record.

The small analyzed groups are relevant to this uncertainty. The primary endpoint analysis included 13 participants per group, and the outcome was met by 3 participants in each group. With binary outcomes, a small count of events or successes can make an estimate sensitive to individual observations. The interval is a more informative guide to precision than the equality of the rounded percentages alone.

For the secondary death result, the recalculated risk difference is 0.143, with a 95% confidence interval from -0.224 to 0.509. This interval also spans zero and has substantial width. The registry's planning illustrations for that secondary outcome are prospective planning examples based on the observed effect and stated assumptions. They do not increase the precision of the present results or represent observed power.

The record does not provide confidence intervals for the listed serious-event counts or for every safety measure. Precision for those figures cannot be assessed from counts alone. More generally, intervals capture sampling uncertainty under the method used, not uncertainty from missing data, outcome measurement, bias, or limitations in study conduct.

12. Analyses Reported by the Sponsor

The registry reports a sponsor analysis comparing the primary endpoint between the placebo and brexanolone groups using a Chi-squared method under Proc Genmod. The reported risk difference is 0.0, with a 95% confidence interval from -31.8 to 31.8 and a reported p-value of 1.000. The unadjusted re-calculation from the posted summary statistics gives a risk difference of 0.0, a 95% confidence interval from -0.324 to 0.324 on the risk-difference scale, and an unadjusted p-value of 1.0.

The results are consistent in their central estimate and in showing no statistically detectable difference in this comparison. The registry indicates no discrepancy between the reported analysis and recalculation. The sponsor's own analysis takes precedence as the reported trial analysis; the recalculation is a check based on summary data, not a replacement for it. The displayed confidence limits are expressed on different scales in the reported analysis and the recalculation, so they should not be compared by their printed magnitudes without accounting for that scale distinction.

Neither analysis establishes that the groups are equivalent. The interval in the sponsor analysis also includes differences in either direction. Details needed to independently reproduce the sponsor model, including a full specification and participant-level data, are not reported in the registry record. The matching central estimates do not resolve limitations arising from the small analysis population or unavailable endpoint data.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary analysis and multiple outcome measures, including two named secondary outcomes. Testing more than one outcome can create a multiplicity problem: in general, the chance of at least one apparently unusual result may rise as more comparisons are made. Statistical plans can address this through methods such as adjusted significance thresholds or an ordered testing strategy. The registry record does not report whether any such approach was planned or used, nor does it state whether the secondary outcomes were intended to support formal claims. The primary result should therefore remain the main efficacy comparison, while secondary findings are interpreted cautiously.

The primary analysis population is described as all randomized participants who initiated study treatment. The registry further says that the analyzed number represents participants with available data. This indicates that the primary outcome analysis did not include every person in the enrollment figure, but the record does not give the reasons for unavailable data or explain the handling of missing outcomes. It does not report imputation, sensitivity analyses, or an alternative analysis population for the primary endpoint. The possible influence of missing data on the estimate therefore cannot be assessed from the registry record.

The death outcome has a different listed analysis denominator from the primary endpoint. The record does not explain the difference, so it should not be assumed to reflect a particular exclusion rule or analysis strategy. No participant-level flow details are reported in the registry record that would clarify how randomization, treatment initiation, outcome availability, and endpoint analysis relate.

In general, an intention-to-treat analysis aims to retain participants in their randomized groups regardless of treatment initiation or adherence. The primary population described in this record is restricted to randomized participants who initiated study treatment, and the registry does not label it as an intention-to-treat analysis. The full statistical analysis plan, details of protocol deviations, and the handling of treatment discontinuation are not reported in the registry record.

Interim analyses, stopping rules, and any adjustments associated with stopping are not reported in the registry record. Since the study status is terminated, the reason for termination and whether it was related to enrollment, safety, feasibility, or another factor are also not reported. These gaps do not establish that a particular bias occurred; they limit the assessment of how analysis choices and missing information might affect interpretation.

14. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: respiratory failure (28.6%), acute respiratory failure (21.4%), encephalopathy (14.3%), septic shock (14.3%), endotracheal intubation (14.3%).

The safety listing reports serious adverse events for groups with 14 participants at risk in each arm, with 8 affected in each arm. It also reports other adverse events for groups with 14 participants at risk, with 11 affected in each arm. These are descriptive counts from the registry record. They do not by themselves establish whether one treatment has a different safety profile, especially without fuller definitions, event timing, severity breakdowns, and statistical uncertainty.

The listed serious-event terms include respiratory failure, acute respiratory failure, encephalopathy, septic shock, endotracheal intubation, and hypoxia. The registry gives percentages for these terms but does not connect the listed terms to a particular treatment group in the information presented. The terms may also describe events that overlap in a participant; the record does not report whether the categories are mutually exclusive. They should not be summed or read as separate people.

The safety listing reports 7 deaths for placebo and 8 for brexanolone, whereas the secondary outcome reports 6 and 8 participants who died through Day 28. The reason for the difference in the placebo counts is not reported in the registry record, so the two listings cannot be reconciled from the available information. These safety summaries are not a substitute for a complete adverse-event analysis or a causal assessment of treatment-related risk.

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

The primary result describes a specific endpoint at a specific time among participants included in the posted analysis: 23.1% in each group were alive and free of respiratory failure at Day 28. The estimated risk difference is 0.0. This is the observed comparison, not a conclusion that the treatments have the same effect in all patients or settings.

The confidence interval is broad and includes both no difference and possible differences in either direction. The result therefore does not establish equivalence, and it does not rule out potentially meaningful differences. A non-significant or high p-value is not proof that an effect is absent. A conclusion about equivalence would require a suitable design and margin, which are not reported in the registry record.

The result also does not isolate the effect on survival from the effect on respiratory failure. The primary endpoint combines both conditions, and component-specific results are not reported. It does not describe time to recovery, duration of ventilation, or outcomes beyond Day 28. Those questions cannot be answered from the primary endpoint result alone.

The secondary death result is distinct from the primary endpoint and is uncertain. The safety listings provide counts and event terms, but do not establish causation or comparative safety. The registry record does not report a result for the named treatment-emergent adverse-event outcome. A complete evaluation of efficacy and safety cannot be based on the primary percentage alone.

The findings are limited to a small, terminated study with primary analyses based on 13 participants per group. The registry does not report the reason for termination, original sample-size assumptions, full statistical analysis plan, or a detailed account of missing endpoint data. These limitations constrain both precision and assessment of potential bias. They do not justify inferring a particular reason for termination or a particular impact of missingness.

Overall, the posted data show equal observed primary percentages and substantial uncertainty around the treatment contrast. They do not establish that brexanolone improves, worsens, or has no effect on the endpoint. The appropriate interpretation is that this record gives an imprecise estimate from the analyzed participants, with important study and reporting details not available in the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why an observed group comparison should be interpreted together with its uncertainty. Equal percentages can look definitive when read alone, but the primary confidence interval is wide and spans effects in either direction. The point estimate answers what was observed in the analyzed groups; the interval conveys how much uncertainty remains about the underlying contrast.

It also shows why endpoint definitions matter. The primary outcome combines survival with freedom from specified respiratory support. That measure is clinically interpretable as a combined status at Day 28, but it does not reveal which component drives the result. Separate component results would answer different questions, and they are not reported in the registry record.

The record also makes the analysis population visible. The primary endpoint uses 13 participants per group, while the registry lists enrollment as 29 and the death outcome uses 14 per group. Without a participant-flow account and missing-data details, readers cannot fully assess how outcome availability affected the estimates. Such differences in analysis denominators deserve attention without assuming a particular explanation.

Finally, the study status and incomplete reporting underscore the distinction between a posted result and a complete statistical record. The registry lists the study as terminated, but its reason, original sample-size justification, multiplicity approach, and full analysis plan are not reported. The planning illustration for the secondary outcome can help frame future design choices, but it is not the trial's own design calculation and is not observed power. These features make the study useful for illustrating careful interpretation of small, uncertain clinical-trial results.

17. Limitations

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

Several limitations are specific to this trial record. The study is listed as terminated, but the reason is not reported in the registry record. The enrollment figure is 29, while the primary endpoint analysis includes 13 participants per group. The registry does not provide a participant flow that explains the transition from enrollment to the analyzed populations or the reason primary endpoint data were unavailable.

The secondary death outcome uses 14 participants per group, different from the primary endpoint analysis. The record does not explain this distinction. A safety listing reports 7 placebo deaths and 8 brexanolone deaths, while the secondary endpoint reports 6 placebo deaths and 8 brexanolone deaths through Day 28. The reason for the difference in the placebo count is not reported, and the safety listing's timeframe and relationship to the secondary outcome are not clarified.

Although the registry lists the treatment-emergent adverse-event outcome, a result for that outcome is not reported in the registry record. The safety summaries include affected counts and serious-event terms but do not provide a complete account of event timing, seriousness by arm, causal assessment, or uncertainty. The serious-event terms are not assigned to treatment groups in the listed summary.

The full statistical analysis plan, original sample-size justification, multiplicity strategy, interim analyses, and stopping rules are not reported in the registry record. The primary analysis is described as including randomized participants who initiated treatment and had available data, but missing-outcome methods and sensitivity analyses are not reported. These omissions limit assessment of the robustness of the estimates and do not permit conclusions about why the study ended or why the analysis counts differ.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study of Brexanolone for Acute Respiratory Distress Syndrome (ARDS) Due to Coronavirus Disease 2019 (COVID-19) — NCT04537806.
• Registry record last updated 2022-08-19; status last verified 2022-08.
• Results first posted 2022-07-27.
• 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.

21. Record Summary

The registry record describes a randomized, triple-masked, parallel Phase 3 study of brexanolone versus matching placebo in participants receiving mechanical ventilation for COVID-19-related ARDS. The primary endpoint was the percentage alive and free of respiratory failure at Day 28. The posted percentages were 23.1% in each group, with a risk difference of 0.0 and a 95% confidence interval from -0.324 to 0.324.

The study is listed as terminated, with enrollment of 29. The primary endpoint analysis included 13 participants per group; the registry describes the analysis population as randomized participants who initiated study treatment and had available outcome data. The reason for termination and details of missing-data handling are not reported in the registry record.

The secondary death comparison is uncertain, and a result for the named treatment-emergent adverse-event outcome is not reported. Safety listings are descriptive and include counts that are not fully reconciled with the secondary death outcome. The record does not establish equivalence or a definitive treatment effect.