Safety and Efficacy of AT-527 in Subjects With Moderate Coronavirus Disease (COVID-19) in a Hospital Setting: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of AT-527 in Subjects With Moderate Coronavirus Disease (COVID-19) in a Hospital Setting (NCT04396106), a randomized phase 2 study. The primary outcome is Proportions (Active vs. Placebo) of Subjects With Progressive Respiratory Insufficiency (PRI) on or Before Day 14..

2. Clinical Question

The clinical question is framed around worsening respiratory support during the study period, rather than only a single measurement of oxygenation. The endpoint scale ranges from normal oxygenation on room air through progressively more intensive support, with death as the highest level. A change across tiers is intended to capture clinically important deterioration in respiratory status, as defined in the registry.

The study also had objectives concerning safety, tolerability, antiviral activity and efficacy. A secondary outcome concerns change from baseline in the amount of SARS-CoV-2 virus RNA by nasopharyngeal swab. The registry record reports two outcome measures and one analysis; it does not provide enough posted results to characterize all those objectives. The results discussed statistically below therefore concern the primary respiratory endpoint and the reported comparison, not a complete evaluation of every study objective.

3. Trial Design

This was a phase 2, randomized, double-blind, placebo-controlled, parallel-group study of AT-527 in subjects with moderate COVID-19 in a hospital setting. The registry describes masking as triple. The stated enrollment was 83, and the study status is terminated. The recorded study start was 2020-05-26 and primary completion was 2022-01-10.

The planned treatment structure had two parts. Part A evaluated AT-527 at 550 mg BID against matching placebo; Part B evaluated AT-527 at 1100 mg BID against matching placebo. Tablets were to be taken orally for 5 days. Local supportive standard of care was allowed in each group. The registry identifies the sponsor as Atea Pharmaceuticals, Inc.

For the primary endpoint, the posted group results include 41 participants and 3 events for AT-527 550 mg BID, and 40 participants and 4 events for its placebo group. Part B has no reported active-arm participants and reports 2 participants and 0 events in its placebo group. The reported comparison is limited to the Part A groups. The registry does not report an estimate comparing the Part B groups, and the empty active arm means that the dose comparison cannot be evaluated from these posted results.

Randomization and masking are design features intended to reduce bias in treatment assignment and outcome assessment. The registry record does not report enough detail to describe the randomization procedure, allocation concealment, or the practical implementation of masking. It also does not report the protocol's original sample-size justification, its planned statistical analysis details, or reasons for termination. These omissions limit how fully the intended design can be compared with the posted results.

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

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat

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: Intent-to-treat

6. Primary Endpoint

The registry lists the primary outcome as Proportions (Active vs. Placebo) of Subjects With Progressive Respiratory Insufficiency (PRI) on or Before Day 14., measured over Day 14.

The primary endpoint is the proportion of participants with progressive respiratory insufficiency on or before Day 14. The registry defines progression as a ≥ 2-tier increase in the respiratory-support methods required to maintain satisfactory oxygenation, specified as SpO2 ≥ 93%, using a 6-tier hierarchy. The hierarchy covers room air, supplemental oxygen at different levels, positive-pressure devices, invasive respiratory support or ECMO, and death.

This is a binary endpoint for the posted analysis: each participant is counted as having or not having the defined event within the stated timeframe. The endpoint is used to represent worsening respiratory support over the study period, rather than treating every level on the scale as a separate outcome. General statistical context: converting a clinical progression rule into an event count permits comparison of event proportions between groups, but the interpretation depends on the clinical definition, the observation window and how missing or incomplete assessments are handled.

The registry gives the analysis population as intent-to-treat. It does not report further operational details about adjudication of respiratory tiers, handling of participants who died or discontinued before Day 14, or the treatment of missing endpoint assessments. Those details matter because they determine how the endpoint rule is applied to individual participants. The endpoint results should therefore be read as the registry's posted event counts and comparison, without assuming unreported assessment procedures.

7. Results Posted in the Registry

• AT-527 - 550 mg BID: 7.3% (3/41) versus 10.0% (4/40) on control; risk difference -2.7 percentage points (95% CI -14.9 to 9.6), risk ratio 0.73 (0.17–3.06); unadjusted two-proportion z-test p = 0.667.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: a participant either meets the registry's definition of progressive respiratory insufficiency by Day 14 or does not. The posted summary gives event counts and group sizes. For the Part A comparison, the recalculated risk difference is the active-group event proportion minus the placebo-group event proportion. A negative value indicates a lower observed proportion in the active group under this convention; it is not a statement about causation beyond the randomized comparison, and it does not by itself establish a reliable treatment effect.

The recalculated risk difference is -0.027. Its 95% confidence interval is -0.149 to 0.096. The interval describes the uncertainty around the estimated difference under the assumptions of that unadjusted calculation. General explanation: a confidence interval is a range of values that are reasonably compatible with the data and the statistical model used to calculate it. It does not mean that the true effect has a particular probability of lying in this specific realized interval. The interval crosses zero, so it does not isolate a single direction of difference.

What does the unadjusted p-value represent?

The unadjusted p-value is 0.667. General explanation: a p-value measures how surprising data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the model assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure the probability that a treatment works. A p-value does not show whether a difference is clinically important, and a large p-value does not prove that the groups are equivalent. The observed event counts and the uncertainty interval remain essential to interpretation.

The term unadjusted distinguishes this recalculation from the registry's reported Cochran-Mantel-Haenszel analysis. The recalculation uses the posted summary counts without adjustment. It should not be read as a substitute for an analysis that might account for strata or other planned design features. The registry reports the method name and p = 0.721 for the Part A groups, but does not report the stratification details, estimated effect, confidence interval, or complete analysis specification. No unreported adjustment can be reconstructed from the method name alone.

Why might two p-values differ?

Different statistical procedures can use the same group data differently. A Cochran-Mantel-Haenszel procedure generally combines comparisons across strata; that is a general description of the method, not a claim about which strata were used in this study. An unadjusted calculation compares the group summaries without such stratification. The registry record does not report the strata or the detailed sponsor analysis specification, so the numerical difference between p = 0.721 and the unadjusted p-value of 0.667 cannot be attributed to a particular design or analysis choice. The posted sponsor analysis remains the registry-reported analysis; the recalculation offers a transparent unadjusted reference based on the summary counts.

The estimate is also affected by the nature of binary data. Each event contributes to the count, and with few events, a small change in the observed count can have a noticeable effect on a proportion or its uncertainty. General statistical context: binary outcomes discard detail about the timing and severity of events beyond the event definition. Here, the endpoint itself uses a tiered respiratory-support scale, but the primary summary reduces that information to whether a participant crossed the defined threshold by Day 14.

What information is missing from the method description?

The registry identifies the primary population as intent-to-treat and identifies the sponsor test as Cochran-Mantel-Haenszel. It does not report the test's strata, the handling of missing or unavailable endpoint assessments, any imputation procedure, or whether the analysis incorporated additional covariates. It also does not report a detailed statistical analysis plan or the protocol's original sample-size justification. Those are not details that can be inferred from the group counts or the reported p-value.

The study was randomized and described as double-blind in its official title; registry masking is recorded as triple. These features address design and conduct, not the mathematical uncertainty in the estimate. Randomization can support a fair comparison in expectation, but it does not ensure that small groups will have balanced characteristics, and masking does not remove uncertainty from sparse outcomes. The posted summary does not include baseline characteristics needed to assess group balance.

Finally, the comparison's scope matters. The primary estimate concerns the 550 mg BID and corresponding placebo groups. The recorded Part B active group has no participants, and its placebo group has 2 participants. No statistical method can yield a useful dose comparison where one corresponding group has no reported participants. The single reported analysis and the absence of posted secondary outcome results further limit how broadly the primary comparison can be interpreted. General statistical explanation should not be mistaken for a claim that any particular unreported procedure was used in this trial.

10. Confidence Intervals and Precision

The confidence interval for the recalculated unadjusted risk difference is -0.149 to 0.096, with a point estimate of -0.027. The interval is important because it makes the uncertainty visible: it covers negative and positive differences, rather than supporting a clear direction. In plain terms, the posted Part A counts are compatible with the active group having a lower event proportion, but they are also compatible with a higher event proportion. The interval does not establish equivalence or rule out a potentially meaningful difference.

General explanation: a confidence interval is wider when the data contain less information or when the outcome is variable, and narrower when the estimate is more precise under the model. The primary endpoint comparison has few events in both groups, which limits precision. The interval's breadth is consistent with uncertainty around the point estimate; it should not be reduced to a single conclusion based only on whether it includes zero.

The registry-reported Cochran-Mantel-Haenszel result is p = 0.721, but no associated confidence interval or effect estimate is reported for that analysis. Its precision therefore cannot be assessed from the reported p-value alone. The unadjusted interval pertains to the recalculated comparison and should not be represented as the interval from the sponsor's analysis.

Precision is also limited by scope. The results with a calculable comparison are for the 550 mg BID Part A groups. The active Part B group reports no participants, and the corresponding placebo group reports 2 participants, so the registry does not support a precise comparison for that dose. The record does not provide confidence intervals for the Part B results or a combined estimate across dose parts.

In general, statistical precision and clinical importance are related but distinct. The interval describes statistical uncertainty around the estimated difference; deciding what range of differences would matter clinically requires information that is not reported in the registry record. No threshold for a clinically important difference is stated.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial's own design calculations. For this binary outcome, the listed figures are participants per arm, not total events. The 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 set at the stated fraction of the observed effect.

The 80% power column means the illustrated number of participants per arm under which the assumed design would have an 80% probability of detecting the specified effect, if the planning assumptions and effect were correct. The 90% power column uses a higher target probability of detecting that effect and therefore has larger participant requirements in the listed rows. These are planning concepts, not guarantees about what a future study would find.

The row for planning for 100% of the observed effect lists 1,724 participants per arm for 80% power and 2,307 participants per arm for 90% power. Planning for 75% of the observed effect lists 3,173 participants per arm for 80% power and 4,247 participants per arm for 90% power. Planning for 50% of the observed effect lists 7,378 participants per arm for 80% power and 9,877 participants per arm for 90% power. The figures increase as the assumed effect becomes smaller: a smaller difference is harder to distinguish from random variation, so more participants are needed under the stated assumptions.

The sample-size curve presents the same general planning relationship visually. Its purpose is to show how required participants per arm vary with the effect used for planning; it does not show observed trial outcomes or actual enrollment. These figures are not observed power. The trial's own original sample-size assumptions and justification are not reported in the registry record, so the planning illustration should not be treated as the protocol's target or evidence that the trial was designed around these figures.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.100; treatment proportion p₁ = 0.073; average p̄ = 0.087.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3977 = 0.7795.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3973 = 0.3343.
4. n = (0.7795 + 0.3343)² / (-0.0268)² = 1,723.6, rounded up to 1,724 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 <- 0.1                          # control proportion
p1 <- 0.0731707317073171                          # 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(4396106)
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 = 1,724 (80% power), 2,307 (90% power)
 75% of observed effect: n per arm = 3,173 (80% power), 4,247 (90% power)
 50% of observed effect: n per arm = 7,378 (80% power), 9,877 (90% power)
power.prop.test: 1723.6 
Simulated power at n = 1,724 per arm: 0.804 (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.

13. Analyses Reported by the Sponsor

The registry reports a Cochran-Mantel-Haenszel analysis comparing the AT-527 550 mg BID group with its placebo group, with p = 0.721. This is the sponsor's reported analysis as recorded in the registry. The registry does not provide an effect estimate, confidence interval, strata description, or complete analysis details alongside that result.

The recalculated unadjusted analysis uses the posted group counts: 3 events among 41 participants in the active group and 4 among 40 in placebo. It gives a risk difference of -0.027, a 95% confidence interval from -0.149 to 0.096, and an unadjusted p-value of 0.667. This calculation is a simple comparison of the posted summary statistics and does not reproduce the sponsor's Cochran-Mantel-Haenszel procedure.

The two p-values are not identical because the analyses are not reported as the same procedure. The record lacks the details needed to explain the difference more specifically. The sponsor's result should be described as the reported analysis, while the recalculation is useful as an unadjusted reference. Neither p-value should be used alone to claim equivalence, benefit, or absence of an effect. Since discrepancy is not flagged in the registry entries, there is no stated conflict that would displace the sponsor's analysis.

14. Multiplicity, Missing Data and Analysis Populations

The trial has multiple stated objectives, including safety, tolerability, antiviral activity and efficacy. The registry lists the primary respiratory endpoint and a secondary outcome concerning change from baseline in the amount of SARS-CoV-2 virus RNA by nasopharyngeal swab. It also reports two outcome measures and one analysis. The posted results available for interpretation include the primary endpoint comparison but do not include results for the secondary viral RNA outcome.

When a study examines multiple outcomes, doses, timepoints or comparisons, the chance of obtaining at least one apparently unusual result can increase if each is interpreted independently. General statistical context: multiplicity procedures can control this issue, but the appropriate approach depends on the prespecified analysis plan and the family of comparisons being considered. Whether a multiplicity adjustment was planned or used is not reported in the registry record. No adjustment should be assumed from the single reported p-value.

The registry describes Part A and Part B with different doses, each with a matching placebo. The posted primary comparison is only for Part A. The active Part B arm reports zero participants, while its placebo group reports 2 participants. The record does not report a combined dose analysis or an analysis of the second dose. The absence of posted Part B results should not be interpreted as a null finding; the comparison is not estimable from these group records.

The endpoint population is identified as intent-to-treat, but the record does not specify how missing endpoint data, early discontinuation, or incomplete follow-up through Day 14 were handled. It also does not report the detailed analysis population for the sponsor's test beyond the endpoint's intent-to-treat designation. These omissions prevent assessment of whether all randomized participants were included in the reported comparison and how unavailable outcomes affected the analysis.

The registry does not report the trial's statistical analysis plan, its original sample-size justification, interim analyses, or multiplicity strategy. These are important distinctions when interpreting a phase 2 study with multiple objectives and dose parts. The reported evidence should therefore be limited to the comparison and analyses actually posted, without inferring prespecified hierarchy, adjustment, or missing-data methods.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pulmonary embolism (50.0%), oxygen saturation decreased (5.0%), abdominal abscess (2.5%), acute kidney injury (2.5%), acute respiratory failure (2.5%).

The registry reports serious adverse events for the groups. For AT-527 550 mg BID, 5 of 40 participants at risk had a serious adverse event; for its placebo group, 3 of 40 had one. The Part B active group reports zero participants at risk and zero serious adverse events, while its placebo group reports 1 of 2 participants at risk with a serious adverse event. These counts describe the posted safety record and should be read separately from the primary efficacy endpoint.

The registry reports deaths of 0 in the AT-527 550 mg BID group, 2 in its placebo group, 0 in the Part B active group and 1 in the Part B placebo group. The Part B group sizes are particularly limited in the posted record, and these counts do not support a stable comparison. The registry lists serious-event terms including Pulmonary embolism at 50.0%, Oxygen saturation decreased at 5.0%, Abdominal abscess at 2.5%, Acute kidney injury at 2.5%, Acute respiratory failure at 2.5% and COVID-19 pneumonia at 2.5%. The denominators and aggregation basis for those term percentages are not reported in the registry record.

General statistical context: safety counts are descriptive, and differences in small groups can be highly uncertain. These figures do not establish that an event was caused by treatment or that groups had comparable risk. The registry record does not provide enough information about event definitions, exposure-adjusted rates or detailed attribution to support further comparative conclusions.

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

The posted results describe a randomized comparison of AT-527 550 mg BID and matching placebo on the proportion of participants with progressive respiratory insufficiency by Day 14. The event counts are 3 among 41 in the active group and 4 among 40 in placebo. The unadjusted estimated risk difference is -0.027, with a 95% confidence interval from -0.149 to 0.096, and the unadjusted p-value is 0.667. The sponsor-reported Cochran-Mantel-Haenszel result is p = 0.721.

These estimates do not show a precise treatment-group difference. The unadjusted interval includes both negative and positive differences, and the event counts are limited. A p-value that is not small does not demonstrate equivalence and does not show that no effect exists. Conversely, the point estimate alone does not establish a treatment effect. The data should be read as uncertain rather than as a definitive positive or negative finding.

The evidence applies to the posted Part A comparison. The registry does not provide an active-versus-placebo result for 1100 mg BID: the active Part B arm reports no participants, and its placebo arm reports 2 participants. The study's secondary viral RNA outcome is listed, but its results are not posted in the registry record described by the registry record. Accordingly, the primary comparison cannot answer every stated objective of the study.

The registry record reports a terminated study and an enrollment of 83, but it does not report the reason for termination or the trial's original design assumptions. It also does not report enough information about missing outcomes, analysis details, or multiplicity to assess those aspects fully. General statistical interpretation should distinguish the posted evidence from unanswered questions: the results characterize the recorded endpoint comparison but do not provide a complete account of all planned doses, outcomes or analysis decisions.

Nothing in these numbers alone establishes whether AT-527 is effective or ineffective, nor do the safety counts establish causation. The result is best understood as a limited and imprecise comparison within the registry record, not as clinical guidance or a conclusive judgment about treatment.

17. Why This Trial Matters Statistically

This trial illustrates why statistical conclusions depend on more than the direction of a point estimate. The observed primary endpoint counts are close, and the unadjusted risk-difference interval ranges from -0.149 to 0.096. That interval conveys substantial uncertainty about both the direction and size of the comparison. Reporting the estimate alongside its interval is more informative than relying on a p-value alone.

It also shows why the analysis method matters. The registry reports a Cochran-Mantel-Haenszel p-value of 0.721, while a simple unadjusted recalculation gives p = 0.667. These values arise from distinct analyses, and the registry does not report enough detail to reconstruct the sponsor's procedure. A responsible reading keeps the reported result and the unadjusted reference distinct instead of treating them as interchangeable.

The dose structure is statistically important. Although the trial description includes two dose parts, the posted active Part B group has no participants and its placebo group has 2. This means that the reported primary comparison cannot answer the question for the 1100 mg BID dose. Stating the existence of a planned group is not the same as having an estimable comparison for that group.

Finally, the sample-size illustration shows how planning requirements depend on the effect chosen for detection: smaller assumed effects require more participants under the stated assumptions. These planning quantities are separate from the trial's original design rationale, which is not reported. Together, the endpoint definition, sparse counts, analysis details and missing planned-dose comparison demonstrate why trial results must be interpreted within the limits of the posted record.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary comparison has few observed events: 3 in the AT-527 550 mg BID group and 4 in its placebo group. This limits the precision of the estimate, as reflected in the unadjusted 95% confidence interval from -0.149 to 0.096. The posted result does not narrowly identify the direction or magnitude of the difference.

The registry describes two dose parts, but the active 1100 mg BID group reports zero participants and the corresponding placebo group reports 2. The Part B comparison therefore cannot be interpreted as a meaningful test of that dose. The Part A result should not be generalized to the unreported active Part B comparison.

The study is marked terminated, but the reason for termination is not reported in the registry record. The registry record also does not report the original sample-size justification, detailed statistical analysis plan, multiplicity strategy, interim analyses, or the specific missing-data procedures. Those omissions prevent a full assessment of whether the posted analysis followed all planned procedures or how missing outcomes could have affected estimates.

The reported sponsor test is identified as Cochran-Mantel-Haenszel, but its strata and detailed implementation are not reported. The recalculated unadjusted comparison is not a replacement for those details. The registry also does not report a sponsor effect estimate and confidence interval for that test, limiting direct comparison of effect magnitude and precision.

Although a secondary viral RNA outcome is listed, its results are not reported in the registry record by the registry record. The record also does not provide baseline characteristics or additional details needed to assess group balance and endpoint assessment. Safety figures are descriptive, and the denominator or aggregation basis for listed serious-event term percentages is not reported. These limitations constrain conclusions to the primary Part A endpoint summary and the posted safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of AT-527 in Subjects With Moderate Coronavirus Disease (COVID-19) in a Hospital Setting — NCT04396106.
• Registry record last updated 2023-03-09; status last verified 2023-02.
• Results first posted 2023-03-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04396106 is a phase 2 randomized, double-blind, placebo-controlled, parallel-group study of AT-527 in adults with moderate COVID-19 in a hospital setting. The planned dose parts were 550 mg BID and 1100 mg BID, each with matching placebo; treatment was described as oral for 5 days, with local supportive standard of care allowed. The registry records enrollment of 83, study status as terminated, a start date of 2020-05-26 and primary completion on 2022-01-10.

The primary endpoint is progressive respiratory insufficiency on or before Day 14. The posted Part A comparison reports 3 events among 41 participants for AT-527 550 mg BID and 4 among 40 for placebo. Its recalculated unadjusted risk difference is -0.027, with a 95% confidence interval from -0.149 to 0.096 and p = 0.667. The registry reports a Cochran-Mantel-Haenszel p-value of 0.721. Part B has no participants reported in the active group and 2 in its placebo group. The record does not report the reason for termination or the original sample-size justification.