Proxalutamide Treatment for Hospitalized COVID-19 Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Proxalutamide Treatment for Hospitalized COVID-19 Patients (NCT04728802), a randomized phase 3 study. The primary outcome is 14 Day Recovery Rate.

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, double-masked, parallel-group phase 3 trial sponsored by Applied Biology, Inc. The study title is Proxalutamide Treatment for Hospitalized COVID-19 Patients. The registry lists enrollment of 645. The recorded study start was 2021-02-01, and primary completion was recorded as 2021-04-15. The trial status is COMPLETED.

Participants were assigned to Proxalutamide + Usual Care or Placebo + Usual Care. Usual care was determined by the care provider in both groups. For the primary endpoint, the posted group summaries give 317 participants and 258 recoveries in the proxalutamide group, and 328 participants and 117 recoveries in the placebo group. These are the endpoint denominators and event counts recorded for the comparison; they do not establish which analysis population was used or how missing outcomes were handled.

Randomization and double masking are important design features: random assignment is intended to reduce systematic differences between groups, while masking can limit some differences in care or outcome assessment. Those design features do not, on their own, establish that every possible source of bias was prevented. The allocation ratio, randomization procedure, concealment method, masking implementation, treatment duration, and details of site conduct are not reported in the registry record.

The record names 28 Day Recovery Rate, 28 Day Mortality Rate, and Post-Randomization Time to Recover (Alive Hospital Discharge) as secondary outcomes. The posted results include numerical summaries for the first two, but no reported analyses are listed for the time-to-recovery endpoint. The original design assumptions and statistical analysis plan are not reported in the registry record, so the posted comparisons should be interpreted as recorded results rather than as a complete account of the trial’s prespecified 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.

Overall Study

Reasons for not completing this period:

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 14 Day Recovery Rate, measured over Day 14.

The primary endpoint is the 14 Day Recovery Rate, measured as the number of participants reaching score 1 or 2 on the COVID-19 ordinal scale over 14 days after randomization. Score 1 means not hospitalized with no limitations on activities; score 2 means not hospitalized with limitations on activities. The remaining scale levels describe hospital status, the need for supplemental oxygen or more intensive respiratory support, and death. The endpoint therefore treats those reaching either of the two stated recovery categories as having the event.

This is a binary endpoint: each participant is classified according to whether the recovery definition was met by the assessment period. Counts and group denominators can be compared directly, and the result can be expressed as a difference between group proportions. That makes the endpoint comparatively straightforward to communicate, although it discards information about intermediate scale levels and the timing or course of recovery. Two participants who do not meet the endpoint may have had different clinical experiences, which the binary summary does not distinguish.

Recovery at a stated follow-up point can be useful for comparing groups on a clinically interpretable status rather than on a laboratory measure alone. That is a general reason such endpoints are used; the registry does not report why this particular endpoint or its score threshold was chosen. The record also does not report how the ordinal scale was assessed, how missing Day 14 status was classified, or whether recovery required a sustained state. Those details matter when interpreting exactly what the event count represents.

7. Results Posted in the Registry

• Placebo + Usual Care: 35.7% (117/328) versus 81.4% (258/317) on control; risk difference -45.7 percentage points (95% CI -52.4 to -39.0), risk ratio 0.44 (0.38–0.51); unadjusted two-proportion z-test p = <0.001.

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.

28 Day Recovery Rate

• 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 + Usual Care: 47.3% (155/328) versus 85.5% (271/317) on control; risk difference -38.2 percentage points (95% CI -44.9 to -31.6), risk ratio 0.55 (0.49–0.63); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo + Usual Care than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

28 Day Mortality Rate

• 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 + Usual Care: 49.4% (162/328) versus 11.0% (35/317) on control; risk difference 38.3 percentage points (95% CI 31.9 to 44.8), risk ratio 4.47 (3.21–6.23); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Placebo + Usual Care than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The two secondary outcomes with posted numerical comparisons follow a directionally coherent pattern with the primary result: the recovery outcome remains higher in the proxalutamide group, and the mortality outcome is higher in the placebo group. Both secondary comparisons have unadjusted p-values of <0.001. This broad alignment is relevant because it shows that the direction of the primary endpoint contrast is not reversed in the posted later recovery and mortality summaries.

The outcomes are related but are not interchangeable. Recovery at a later assessment describes status at that time, while mortality records a different event. The registry also lists post-randomization time to recover among participants discharged alive, which would address timing, but it contains no reported analysis for that endpoint. The posted summaries do not establish how these outcomes were jointly analyzed or whether they represent independent evidence.

Secondary endpoints generally provide context about other aspects of the trial, but their interpretation depends on how many outcomes and analyses were considered and whether a testing hierarchy or multiplicity adjustment was prespecified. Those details are not reported in the registry record, and the posted secondary p-values are unadjusted. Consequently, the secondary results should carry less confirmatory weight than a primary outcome interpreted under a prespecified analysis plan. They can be described as consistent with the primary pattern, but they should not be treated as multiple independent proofs of the same conclusion.

The registry lists 28 Day Recovery Rate, 28 Day Mortality Rate, and Post-Randomization Time to Recover (Alive Hospital Discharge) as secondary outcomes. Numerical comparisons are posted for the first two, but no reported analyses are listed for the time-to-recovery outcome. The record does not explain why numerical analyses are absent for that endpoint, whether it was not analyzed, or whether results were collected but not posted. That uncertainty makes the available secondary evidence incomplete.

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

• 28 Day Recovery Rate
• 28 Day Mortality Rate
• Post-Randomization Time to Recover (Alive Hospital Discharge)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant reached the specified recovery status by Day 14. For a binary endpoint, a group proportion is the event count divided by the number of participants in that group. The posted summaries give the event counts, denominators, and proportions directly. The comparison reported for this endpoint is a risk difference: the proportion in the placebo group minus the proportion in the proxalutamide group. A negative value therefore indicates a lower observed recovery proportion in the placebo group for this coding of the comparison.

What does the risk difference express?

A risk difference expresses an absolute contrast in event proportions, rather than a relative contrast. It is measured on the same proportion scale as the outcome. Its sign depends on the order in which groups are subtracted, so the group ordering should always be checked before interpreting a positive or negative estimate. Here, the posted estimates and group proportions show the direction of the Day 14 recovery comparison. The risk difference does not, by itself, adjust for other variables; whether any adjusted analysis was planned or performed is not reported in the registry record.

How should the confidence interval be read?

A confidence interval conveys the precision of an estimated contrast under the method used to construct it. In repeated use of the same procedure under its assumptions, intervals produced in that way would cover the underlying value at the stated rate. It is not a guarantee that the true value lies within this particular interval, and it does not account for every design or reporting limitation. For the primary outcome, the reported 95% confidence interval is -0.524 to -0.390. Both limits are negative, so the interval excludes a risk difference of zero under the reported scale and method.

What does the p-value add?

The unadjusted p-value for the primary comparison is <0.001. A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the result arose by chance, nor is it a measure of clinical importance. Interpretation also depends on the test and assumptions used. The registry record does not report the full test specification or analysis plan, so the posted p-value should be understood as an unadjusted result rather than as a complete inferential framework.

Why does the binary endpoint matter?

Reducing an ordinal scale to a binary recovery definition makes the comparison easy to express as event counts and proportions. However, it leaves out distinctions among participants who did not reach scores 1 or 2. It also does not show when within the assessment period recovery occurred. A time-to-event analysis can address timing, but the registry lists post-randomization time to recover as a secondary outcome without a reported numerical analysis. The endpoint definition, assessment procedures, and handling of participants whose status was unavailable are important to interpretation and are not fully described in the registry record.

What can and cannot be inferred from randomization?

Random allocation is intended to make treatment groups comparable on average, including on factors that were not measured. Double masking can reduce the possibility that knowledge of assignment changes care or assessment. These are general design advantages, not proof that all sources of bias are absent. The registry identifies the design as randomized and double-masked but does not report sequence generation, concealment, implementation details, or whether masking was maintained. Nor does it report the analysis population, protocol deviations, or missingness by group. Those omissions limit independent assessment of how the design translated into the posted analysis.

How should the secondary analyses be treated?

The posted 28 Day Recovery Rate and 28 Day Mortality Rate comparisons are also binary outcomes and use risk differences. Their unadjusted p-values are both <0.001. Multiple outcomes create multiple opportunities to observe a small p-value, particularly when outcomes or analyses are selected after results are known. A prespecified multiplicity strategy can control the interpretation of a family of tests, but such a strategy is not reported in the registry record. The registry lists three secondary outcomes, while numerical results are posted for two; no reported analysis is listed for the time-to-recovery outcome. Without a reported analysis plan, the secondary findings are best viewed as supportive descriptive evidence rather than as a separate confirmatory testing program.

What do the planning illustrations represent?

The sample-size illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. For binary outcomes, the figures are participants per arm. These are planning illustrations based on the observed results, not the original trial’s sample-size justification. They are not observed power. The registry does not report the trial’s original design assumptions or sample-size calculation.

Planning estimates depend on assumptions about the underlying event proportions, effect size, allocation, statistical test, and desired operating characteristics. They should not be interpreted as showing that the completed trial had a particular probability of detecting an effect after the results were observed. The figures illustrate how required enrollment changes when the effect assumed for planning is varied, under the stated approximation. More modest effects generally require more participants for the same target power.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.457, with a reported 95% confidence interval from -0.524 to -0.390. The interval is entirely below zero, so the estimated difference is directionally consistent across its endpoints when the contrast is coded as placebo plus usual care minus proxalutamide plus usual care. Its width describes uncertainty around the estimated group contrast under the interval method; it is not a range for individual outcomes or a prediction interval for a future trial.

Precision is influenced by the number of observed events, group sizes, outcome variability, and the analysis method. A confidence interval can be narrow while important design or measurement uncertainties remain. In particular, the registry does not report missing-outcome handling, the analysis population, or details of the statistical procedure used to obtain the interval. The interval therefore characterizes sampling uncertainty under the reported analysis, not uncertainty from all possible sources.

For context, the posted secondary risk differences are -0.382 for 28 Day Recovery Rate, with a 95% confidence interval from -0.449 to -0.316, and 0.384 for 28 Day Mortality Rate, with a 95% confidence interval from 0.319 to 0.448. Their signs reflect the reported comparison ordering, with placebo relative to proxalutamide. These intervals also exclude zero, but the secondary analyses are unadjusted and should be interpreted in light of multiplicity and the absent analysis plan.

Confidence intervals are more informative than a threshold alone because they communicate both direction and a range of plausible contrasts. They do not indicate whether an effect is important in practice, and the registry does not provide a prespecified threshold for interpreting the magnitude of a difference. The displayed precision should be read alongside the endpoint definition, trial design, and unreported analysis details.

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 report participants per arm for the binary outcomes. They do not report total events. The assumptions listed for these illustrations 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 to the stated fraction of the observed effect. These assumptions describe the planning illustrations, not the original design justification for the trial; the original design assumptions are not reported in the registry record.

For the primary Day 14 recovery comparison, planning for 100% of the observed effect gives 18 participants per arm for 80% power and 23 participants per arm for 90% power. Planning for 75% of the observed effect gives 30 participants per arm for 80% power and 39 participants per arm for 90% power. Planning for 50% of the observed effect gives 62 participants per arm for 80% power and 83 participants per arm for 90% power.

The 80% power column means the illustrated design would have an 80% chance of detecting the assumed effect at the stated significance level if the planning assumptions and effect were correct. The 90% column represents a higher target chance of detection under those same assumptions. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm to reach a given power target. These figures are planning illustrations based on the observed effect, not observed power; they do not describe the probability that the completed trial’s result is true or that its analysis would be significant in another study.

The curve should be read as a visual display of how the planning requirement changes with the effect being targeted. Its interpretation depends on the stated assumptions, and it does not replace the original protocol’s sample-size rationale, which is not reported in the registry record.

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 = 0.814; treatment proportion p₁ = 0.357; average p̄ = 0.585.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6967 = 1.3656.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6172 = 0.5195.
4. n = (1.3656 + 0.5195)² / (-0.4572)² = 17.0, rounded up to 18 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 <- 0.813880126182965                          # control proportion
p1 <- 0.356707317073171                          # 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(4728802)
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 = 18 (80% power), 23 (90% power)
 75% of observed effect: n per arm = 30 (80% power), 39 (90% power)
 50% of observed effect: n per arm = 62 (80% power), 83 (90% power)
power.prop.test: 17 
Simulated power at n = 18 per arm: 0.851 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or analytic choices are tested. Even when each individual test uses a conventional significance threshold, considering many tests increases the chance that at least one result will appear unusually strong under a no-effect setting. Prespecified approaches—such as a testing hierarchy or an adjustment across a defined family of outcomes—can guide interpretation. The statistical plan and any multiplicity procedure are not reported in the registry record.

The primary comparison has an unadjusted p-value of <0.001, and the two posted secondary comparisons also have unadjusted p-values of <0.001. The record does not say whether the primary endpoint was the sole confirmatory test, how the secondary outcomes were prioritized, or whether other analyses were performed. Although the registry lists four outcome measures and three secondary outcomes, it does not provide enough information to establish the full family of planned tests. The numerical results should therefore be distinguished from a multiplicity-controlled confirmatory analysis.

Missing-data handling is also not reported in the registry record. The posted endpoint summaries give denominators for both groups, but they do not explain whether those denominators represent everyone randomized, participants assessed at follow-up, or another analysis population. The record does not state how missing Day 14 or later status was handled, whether any imputation was used, or whether sensitivity analyses assessed alternative assumptions. This matters because classification of unavailable outcomes can affect event proportions and treatment comparisons.

The registry does not identify an intention-to-treat, modified intention-to-treat, per-protocol, or safety population for the posted efficacy comparisons. It also does not report exclusions after randomization, adherence, protocol deviations, or whether any participants were analyzed in a group different from their assignment. Those details are necessary to understand how closely the posted comparisons preserve the randomized design.

These absences do not show that the analyses were improperly conducted; they limit what can be verified from the registry record. A full assessment would require the protocol and statistical analysis plan, together with reporting of analysis populations, missingness, and any adjustment for multiple testing.

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: death (49.4%), mechanical ventilation (12.5%).

The posted safety summaries list 38 serious adverse events among 317 participants at risk in the Proxalutamide + Usual Care group and 170 among 328 at risk in the Placebo + Usual Care group. For other adverse events, the corresponding figures are 51 among 317 and 11 among 328. The registry also lists deaths as 35 and 162, respectively. These are counts as recorded in the safety summary; they should not be added together because the categories may overlap, and the record does not describe overlap or event-level counting rules.

The serious adverse event terms listed most prominently are Death at 49.4% and Mechanical Ventilation at 12.5%. The denominator and method behind these percentages are not reported in the registry record. Definitions of serious adverse events, collection period, severity grading, relatedness assessment, and handling of repeated events are also not reported. The group counts therefore provide a descriptive safety summary, but do not by themselves support a complete comparison of event rates or causal attribution. They should be interpreted alongside the posted outcome results and the missing detail on safety methods.

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

The posted Day 14 results show a substantial separation in the observed recovery proportions between the randomized groups, with the confidence interval for the reported risk difference entirely below zero when the comparison is expressed as placebo minus proxalutamide. The unadjusted p-value is <0.001. These statistics describe the trial’s recorded endpoint comparison and its sampling precision under the analysis used.

They do not establish that every participant experienced the same course, because the endpoint collapses the ordinal scale into whether a participant reached score 1 or 2 by the stated follow-up. They do not show the exact timing of recovery, the distribution of intermediate states, or the course of participants who did not reach the recovery threshold. The listed time-to-recovery outcome has no reported analysis in the registry record.

The findings also do not settle questions that depend on information absent from the record. The analysis population, missing-data approach, outcome assessment procedures, original sample-size rationale, and multiplicity strategy are not reported. The observed contrast is therefore not a substitute for a complete evaluation of the protocol, analysis plan, and full trial report. Randomization and double masking are design strengths, but the registry description alone cannot confirm all implementation details or exclude all sources of bias.

Nor should the result be generalized automatically beyond the study population and setting. The summary identifies hospitalized male and female COVID-19 patients, but detailed eligibility criteria and setting information are not reported. The record does not establish whether the same estimate applies in other populations, under other standards of usual care, or at different points in the course of illness.

The statistical result is evidence about a defined comparison in this completed trial. It is not individualized medical guidance, and it does not alone determine the balance of benefits and harms. The safety record includes serious adverse event and death counts, but details needed for a complete safety analysis are also absent.

17. Why This Trial Matters Statistically

This trial is statistically notable because the registry reports a randomized, double-masked comparison and a clear difference in the primary binary outcome, accompanied by a confidence interval that excludes no difference. The outcome is clinically interpretable in broad terms—reaching a defined status outside hospital by Day 14—while still illustrating a common analytic trade-off: converting an ordinal scale into a binary endpoint simplifies comparison but discards distinctions among other health states and the timing of change.

The contrast can be read using an absolute measure, the risk difference, which makes the group separation accessible without relying only on a relative measure or a thresholded p-value. The confidence interval adds information about precision, while the unadjusted p-value addresses compatibility with a no-difference null model under the test assumptions. Considering these statistics together is more informative than treating statistical significance as a complete interpretation.

The trial also highlights why registry-level results need methodological context. The design is identified as randomized and double-masked, but analysis populations, missing-data methods, multiplicity handling, and the original design assumptions are not reported. The secondary findings are directionally aligned with the primary result, yet their unadjusted status and the absence of a reported plan limit their confirmatory role. These distinctions are central to judging how much weight to place on a set of otherwise consistent outcomes.

Finally, the posted planning illustrations show how sample-size requirements vary when the assumed target effect is reduced. They are useful for understanding prospective planning under stated assumptions, but they cannot be recast as observed power or as evidence about the original design rationale. Separating planning calculations from the trial’s actual prespecified design is an important part of sound statistical interpretation.

18. Limitations

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

Several limitations are specific to the information recorded for this trial. The primary endpoint is a binary classification derived from an ordinal scale. It combines score 1 and score 2 as recovery and does not report the distribution across other scores. Consequently, the posted endpoint cannot show whether participants who did not meet the recovery definition were hospitalized without oxygen, required respiratory support, or had another outcome.

The registry record does not report the detailed eligibility criteria, treatment dose or duration, study locations, or the procedures used to assess the ordinal scale. It also does not explain whether the Day 14 recovery status had to be sustained, how participants with missing assessments were treated, or what analysis population produced the posted denominators. These omissions constrain assessment of endpoint implementation and potential bias.

The record does not report the protocol’s original sample-size assumptions, the statistical analysis plan, an approach to multiplicity, or whether any interim analyses were planned or conducted. It lists three secondary outcomes but supplies no reported analysis for post-randomization time to recover among participants discharged alive. Safety summaries lack definitions and information on event overlap, collection procedures, and the denominators behind the listed leading serious adverse event percentages.

The trial is recorded as randomized and double-masked, but methods for allocation concealment and masking implementation are not described. These are reporting limitations in the registry record; they should not be interpreted as evidence that the procedures were absent. A full publication or trial report may contain additional information, but such material is not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Proxalutamide Treatment for Hospitalized COVID-19 Patients — NCT04728802.
• Registry record last updated 2021-06-24; status last verified 2021-06.
• Results first posted 2021-06-23.
• 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 randomized, double-masked, parallel-group phase 3 trial sponsored by Applied Biology, Inc., comparing Proxalutamide + Usual Care with Placebo + Usual Care in hospitalized COVID-19 patients. Enrollment is listed as 645. The recorded start date is 2021-02-01, and primary completion is 2021-04-15.

The primary endpoint is recovery by Day 14, defined as reaching score 1 or 2 on the COVID-19 ordinal scale. The posted group summaries are 258 of 317 participants in the proxalutamide group and 117 of 328 in the placebo group. The reported risk difference is -0.457, with a 95% confidence interval from -0.524 to -0.390 and an unadjusted p-value of <0.001.

Numerical results are also posted for Day 28 recovery and 28 Day Mortality Rate. No reported analysis is listed for post-randomization time to recover among participants discharged alive. The registry does not report the full analysis plan, missing-data methods, or multiplicity approach.