A Study of Rivaroxaban to Reduce the Risk of Major Venous and Arterial Thrombotic Events, Hospitalization and Death in Medically Ill Outpatients With Acute, Symptomatic Coronavirus Disease 2019 (COVID-19) Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Rivaroxaban to Reduce the Risk of Major Venous and Arterial Thrombotic Events, Hospitalization and Death in Medically Ill Outpatients With Acute, Symptomatic Coronavirus Disease 2019 (COVID-19) Infection (NCT04508023), a randomized phase 3 study. The primary outcome is Number of Participants With Time to First Occurrence of Primary Efficacy Composite Endpoint.

2. Clinical Question

The question combines several clinically distinct events in one endpoint. A participant is counted at the first occurrence of any listed component; later components do not create additional primary endpoint events for that participant. This structure allows the trial to assess a broader outcome than any single component alone, but it also means that the overall comparison does not by itself establish what happened for each component separately.

The registry describes the study as evaluating whether rivaroxaban reduces the risk of the composite compared with placebo. That is the study question, not a conclusion about the result. The posted comparison is based on event counts and a time-to-event analysis, and its precision is important when judging what the data can distinguish.

3. Trial Design

This is a randomized, double-masked, parallel-group Phase 3 study sponsored by Janssen Research & Development, LLC. Its listed condition is Coronavirus Disease 2019 (COVID-19). The treatment groups were rivaroxaban 10 mg once daily plus standard of care and matching placebo once daily plus standard of care, with treatment planned for 35 Days. The registry lists an enrollment of 1284.

The study started on 2020-08-13, and the primary completion date is 2022-06-01. Its current status is terminated. The reason for termination, the timing of the termination decision, and whether termination changed the planned analyses are not reported in the registry record. These details matter because the status alone does not explain why the study ended or what consequences that had for interpretation.

The primary endpoint is defined as time from randomization to the first occurrence of any component of the composite, with the endpoint timeframe listed as Up to Day 35. The primary population includes all randomized participants who provided informed consent. The two posted arm counts for this endpoint are 641 in the rivaroxaban group and 643 in the placebo group.

Although the registry calls the study pragmatic, details about the operational features that make it pragmatic are not reported in the registry record. The protocol’s planned sample-size assumptions, original power target, allocation ratio justification, and intended handling of missing outcome data are also not reported. The planning illustrations associated with the posted outcomes are calculations based on observed effects and should be distinguished from the trial’s original design.

The registry lists standard of care in addition to the two randomized treatment groups. The arm descriptions specify that both groups received standard of care; the principal contrast is therefore the addition of rivaroxaban versus matching placebo within that background care. Details of the standard-of-care components and whether they varied among participants are not reported in the registry record.

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: Participants who were not treated with study drug were still followed-up as per the planned visits.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-To-Treat (ITT) analysis set included all randomized participants who provided informed consent.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Time to First Occurrence of Primary Efficacy Composite Endpoint, measured over Up to Day 35.

The primary endpoint is the time from randomization to the first occurrence of any one of seven events: symptomatic venous thromboembolism (VTE), myocardial infarction (MI), ischemic stroke, acute limb ischemia, non-central nervous system systemic embolization, all-cause hospitalization, or all-cause mortality. The registry reports the number of participants who experienced the composite through Day 35, while the endpoint definition also identifies the time to first event as the outcome of interest.

A composite endpoint is used to combine several possible outcomes into one prespecified measure. In general, this can capture more kinds of clinically important events than a single-event endpoint and can provide one overall comparison for the treatment groups. The components do not necessarily have equal severity or occur with equal frequency, however. A composite result can be influenced more by its more frequent components, and the combined estimate does not show which components contributed to the observed events.

The event count is 22 participants among 641 assigned to rivaroxaban and 19 among 643 assigned to placebo. These counts describe participants with a first primary endpoint event, not the total number of component events. Component-specific event counts and results are not reported in the registry record. Consequently, the posted primary result addresses the composite as a whole and does not permit a separate conclusion about each listed event.

Hospitalization and death are included alongside thrombotic events. This broadens the endpoint beyond thrombosis alone, but it also means that the composite should be interpreted according to its full definition rather than as a direct measure of any one type of event.

7. Results Posted in the Registry

• Rivaroxaban 10 Milligrams (mg): 3.4% (22/641) versus 3.0% (19/643) on control; risk difference 0.5 percentage points (95% CI -1.4 to 2.4), risk ratio 1.16 (0.63–2.12); unadjusted two-proportion z-test p = 0.627.

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 With Time to First Occurrence of Major Bleeding Based on a Modification of the ISTH Criteria

• 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:
  • Rivaroxaban 10 Milligrams (mg): 0.2% (1/599) versus 0.0% (0/598) on control; risk difference 0.2 percentage points (95% CI -0.2 to 0.5); unadjusted two-proportion z-test p = 0.318.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rivaroxaban 10 Milligrams (mg) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Were Hospitalized or Dead on Day 35

• 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:
  • Rivaroxaban 10 Milligrams (mg): 0.8% (5/641) versus 0.5% (3/643) on control; risk difference 0.3 percentage points (95% CI -0.5 to 1.2), risk ratio 1.67 (0.40–6.97); unadjusted two-proportion z-test p = 0.475.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rivaroxaban 10 Milligrams (mg) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover time to first occurrence of secondary efficacy outcomes, major bleeding under a modified ISTH definition, and hospitalization or death on Day 35. The available results are limited: participant counts and comparison information are posted for major bleeding and hospitalization or death, while results for the secondary efficacy outcome are not reported in the registry record.

Across the two secondary outcomes with posted comparisons, the estimates do not provide a clear separation between groups. Their point estimates are on the side of more events with rivaroxaban, but the event counts are sparse and the uncertainty intervals include no difference. These outcomes therefore do not materially clarify the uncertain primary result. They also measure different aspects of outcome and safety, so they should not be treated as direct substitutes for the primary composite.

The secondary outcomes are exploratory in interpretation unless the registry documents a prespecified multiplicity procedure. No adjustment for multiple comparisons is reported in the registry record. When several outcomes are examined, the chance of at least one apparently notable finding can increase; without a stated adjustment or hierarchy, individual unadjusted tests carry less weight than a prespecified primary analysis. The registry lists one primary analysis, but it does not describe a broader testing strategy for the secondary outcomes.

These results can be useful as descriptive context, especially for understanding what was measured beyond the primary endpoint. They should not be read as confirmatory evidence on their own. Component-specific results for the primary composite and the full secondary efficacy findings would be needed for a more complete picture, and those details are not reported in the registry record.

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

• Number of Participants With Time to the First Occurrence of Secondary Efficacy Outcomes
• Number of Participants With Time to First Occurrence of Major Bleeding Based on a Modification of the ISTH Criteria
• Number of Participants Who Were Hospitalized or Dead on Day 35

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint combines a participant count with a time-to-event definition. Each participant contributes the time from randomization until the first qualifying component event, if one occurs during the endpoint timeframe. The posted count tells how many participants had such an event. A time-to-event method can additionally use information about when events occurred, rather than treating every event as if it happened at the same time.

What the reported analysis estimates

The registry reports a Log Rank analysis with a Cox Proportional Hazard parameter. The Cox model is a common method for comparing event hazards between groups over follow-up. A hazard describes the instantaneous rate of event occurrence among participants who have not yet had an event, at a particular point in follow-up. A hazard ratio compares those rates between groups under the model. It is not the same quantity as the difference between the proportions who experienced an event by the end of follow-up.

The reported hazard ratio is 1.16, with a 95% confidence interval from 0.63 to 2.15 and p = 0.626. The interval includes 1, the value associated with equal hazards under this measure. The registry’s analysis is classified as a superiority analysis. The registry record does not report details such as model covariates, proportional-hazards diagnostics, or the handling of censoring beyond identifying the Log Rank and Cox methods.

What the recalculation estimates

The recalculation uses the posted event counts and arm sizes to estimate an unadjusted risk difference. In general, a risk difference is the event proportion in one group minus the event proportion in the comparison group. It describes the absolute separation between the observed group proportions over the stated follow-up, rather than comparing event timing or hazards. The recalculated p-value is 0.627, and the confidence interval includes no difference.

This recalculation is intentionally simple. It does not reproduce the sponsor’s time-to-event model, account for event timing, or adjust for other variables. It is useful as a check on the direction and broad scale of the posted counts, but it does not replace the registry’s reported analysis. The two approaches can yield slightly different estimates and p-values because they use different outcome summaries and methods.

How to understand the p-value

A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Here, the reported p-value does not provide strong evidence against equal hazards. It does not prove equality or rule out effects that the confidence interval still allows.

How to understand the confidence interval

A confidence interval describes the uncertainty around an estimate under the statistical method used. In repeated comparable studies, intervals constructed by the same procedure would have a stated long-run coverage property if the assumptions held. For an individual study, it is most useful as a range of effect values reasonably compatible with the data and method. A wide interval signals limited precision; whether any particular value in the interval matters clinically requires context beyond the estimate itself.

Why event counts and follow-up matter

Time-to-event methods are useful when participants may experience an event at different times or may not have an event during observation. They can use timing information and account for differing observed follow-up, subject to the model and censoring assumptions. The registry record does not provide enough detail to assess those assumptions or the amount of follow-up information available for each participant. The primary timeframe is listed as Up to Day 35.

The primary endpoint is a composite, so the method evaluates the first occurrence of any component. That can be statistically efficient in general when multiple relevant events are combined, but interpretation depends on the components and their frequencies. Because component-specific results are not reported in the registry record, the contribution of each component cannot be assessed from the posted primary result.

Finally, the registry identifies an ITT population as all randomized participants who provided informed consent. ITT analysis generally preserves the comparison created by random assignment by analyzing participants according to their assigned group. The record gives this population definition but does not report further detail on exclusions, missing outcomes, or whether every randomized participant contributed to each endpoint analysis.

11. Confidence Intervals and Precision

The reported primary hazard ratio is 1.16, with a 95% confidence interval from 0.63 to 2.15. Because the interval includes 1, the data are compatible with equal hazards as well as with effects in either direction. Its breadth indicates that the estimate is not precise enough to distinguish among a range of potentially different relative effects.

The unadjusted risk-difference interval also includes no difference. This is consistent with the reported time-to-event result in the limited sense that neither analysis yields a clear separation between groups. The two intervals are not directly comparable, because they describe different effect measures. The hazard-ratio interval concerns relative event hazards over time; the risk-difference interval concerns the absolute contrast in observed event proportions.

Confidence intervals are more informative than a binary significant-or-not label because they show the range of estimates compatible with the data under the method. They do not mean that every value inside the interval is equally likely, and they do not guarantee that the true effect lies inside the interval. Their interpretation also depends on the analysis assumptions, which are not fully described in the registry record.

The relatively small number of primary events contributes to uncertainty: there were 22 events in the rivaroxaban group and 19 in the placebo group. The study’s enrollment was 1284, but the amount of information about a time-to-event effect depends substantially on observed events and follow-up, not only on the number randomized. The posted summary does not include enough information to evaluate follow-up completeness or event timing in detail.

Thus, the point estimate should not be read in isolation as a settled treatment contrast. The interval and event counts show that the primary result is uncertain. The registry record does not report a prespecified threshold for a clinically important difference, so statistical precision alone cannot establish whether the range of compatible effects would be important in practice.

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 figures are illustrations based on the observed effect, not the original design calculations for this trial. For this binary endpoint, the listed figures are participants per arm, not total events. The calculation 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 defined as the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the assumptions held. The 90% power column uses the same idea with a higher chance of detecting the specified effect, so it generally requires more participants per arm. These are planning quantities, not descriptions of the trial’s observed results.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. As the effect used for planning becomes smaller, the required number of participants rises. A subtler difference is harder to distinguish from random variation, so more information is needed to detect it with the same nominal power.

For the primary endpoint, the illustration lists 21,307 participants per arm for 80% power and 28,524 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 37,195 and 49,793 participants per arm; for 50%, they are 82,148 and 109,972. These figures should not be interpreted as enrollment targets endorsed by the trial or as evidence about the power achieved in the completed study.

This is not observed power. Observed power calculated from an estimated effect largely restates the observed result and does not resolve uncertainty. The useful reading is prospective and conditional: the figures illustrate how sample requirements change under stated assumptions and effect sizes. The registry’s own original sample-size justification and design assumptions are 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 = 0.030; treatment proportion p₁ = 0.034; average p̄ = 0.032.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2487 = 0.4874.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2486 = 0.2093.
4. n = (0.4874 + 0.2093)² / (0.0048)² = 21,306.7, rounded up to 21,307 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 <- 0.0295489891135303                          # control proportion
p1 <- 0.0343213728549142                          # 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(4508023)
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 = 21,307 (80% power), 28,524 (90% power)
 75% of observed effect: n per arm = 37,195 (80% power), 49,793 (90% power)
 50% of observed effect: n per arm = 82,148 (80% power), 109,972 (90% power)
power.prop.test: 21306.7 
Simulated power at n = 21,307 per arm: 0.800 (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. Analyses Reported by the Sponsor

The registry’s reported primary analysis is the sponsor-reported time-to-event analysis: a Log Rank test and Cox Proportional Hazard estimate. It gives a hazard ratio of 1.16, a 95% confidence interval from 0.63 to 2.15, and p = 0.626. This is the analysis to use when describing the trial’s posted primary result.

The recalculation is a simple, unadjusted comparison of the posted participant counts. It uses a risk difference rather than the sponsor’s time-to-event hazard ratio and gives p = 0.627. The p-values are close, and both analyses leave the no-difference value within their respective confidence intervals. This broad agreement does not make the methods interchangeable: one uses event timing and a hazard model, while the other summarizes the observed proportions.

The recalculation is a transparent way to check the broad pattern in the counts, but it does not supersede the reported analysis. It does not account for timing or reproduce the Cox model. The registry record does not report further model specifications that would allow an independent reconstruction of the sponsor’s time-to-event result. There is no posted discrepancy flag for the primary result.

Accordingly, the sponsor’s reported estimate and test should anchor the description of the primary analysis; the recalculation serves as a complementary unadjusted summary. Neither establishes a clear treatment-group difference, and neither removes the uncertainty reflected in the confidence intervals.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary analysis and three secondary outcomes, but it does not report a multiplicity adjustment or a formal hierarchy for testing the secondary outcomes. Multiplicity arises when several hypotheses are examined: even if no true differences exist, conducting many tests can make at least one result appear notable by chance. Procedures such as prespecified testing sequences or adjusted significance thresholds can address that issue, but no such procedure is described in the registry record.

The reported primary p-value should therefore be distinguished from any unadjusted secondary p-values. The available secondary comparisons are descriptive and do not have a reported multiplicity strategy that would support treating them as confirmatory. This does not invalidate their role as observations, but it limits the strength of claims based on individual secondary tests.

The primary population is described as the ITT analysis set, including all randomized participants who provided informed consent. The registry posts 641 participants in the rivaroxaban arm and 643 in the placebo arm for the primary endpoint. Safety summaries use denominators of 599 and 598, respectively. The reason for the difference between these outcome-specific populations and the primary randomized counts is not reported in the registry record.

Missing-data methods are not reported in the registry record. In particular, the record does not explain how participants without complete endpoint follow-up were handled, what censoring rules were used, whether any sensitivity analyses were conducted, or how missing component information was treated. Such details are relevant to interpreting time-to-event estimates and the robustness of the results.

The registry does not report interim analyses, stopping rules, detailed model covariates, or the original sample-size justification. These omissions do not establish that such procedures were or were not used; they mean the posted record does not allow their role to be assessed. The terminated status is listed, but the reason and any implications for multiplicity or analysis decisions are not reported.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: drug hypersensitivity (0.2%).

The registry’s safety summary lists serious adverse events for 599 participants at risk in the rivaroxaban group and 598 in the placebo group. One participant in the rivaroxaban group and none in the placebo group are listed as affected by a serious adverse event. The top serious adverse event term is Drug Hypersensitivity, listed as 0.2%. The summary also lists 57 participants with other adverse events in the rivaroxaban group and 50 in the placebo group, with 2 deaths in each group.

These figures are descriptive counts. The safety denominators differ from the primary endpoint arm counts, and the registry record does not explain the population selection or provide additional detail about exposure, event timing, severity beyond the serious-event classification, or causal attribution. A count recorded during a trial does not by itself establish that the assigned treatment caused the event.

The number of serious events is small, so the posted counts offer limited precision for comparing uncommon harms. They should be read alongside the trial’s design and the limited detail available in the registry record, rather than interpreted as a complete assessment of safety. No medical conclusion can be drawn from these counts alone.

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

The posted data show similar observed numbers of participants with the primary composite event in the two randomized groups: 22 with rivaroxaban and 19 with placebo. The sponsor-reported time-to-event estimate is 1.16, but its 95% confidence interval from 0.63 to 2.15 is wide and includes equal hazards. The reported p-value is 0.626. Taken together, these results do not demonstrate a clear difference between the groups in the primary endpoint.

That interpretation is not the same as concluding that the treatments have identical effects. The confidence interval remains compatible with effects in either direction, and the trial had relatively few primary events. The estimate is therefore imprecise. A result that does not meet a conventional significance threshold cannot be used as proof of no effect or as proof of equivalence; equivalence requires its own design, margin, and analysis, none of which is reported in the registry record.

The primary result concerns a composite endpoint through Day 35. It does not separately answer questions about VTE, myocardial infarction, stroke, limb ischemia, systemic embolization, hospitalization, or mortality. Nor does it establish effects beyond the listed endpoint timeframe. Component-specific primary results and longer-term findings are not reported in the registry record.

The secondary outcomes provide limited additional context, and the registry does not report a multiplicity procedure for their interpretation. Safety counts are also sparse and descriptive. Neither the secondary nor safety summaries remove the uncertainty around the primary estimate.

The study status is terminated, but the reason is not reported in the registry record. The status alone cannot be used to infer why the trial ended or to explain its result. The appropriate conclusion is limited to the posted comparisons: the observed data do not clearly distinguish the groups, and the available precision and reporting leave important questions unresolved.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through both its estimate and its uncertainty. The event counts are close, the reported hazard ratio is 1.16, and the confidence interval extends across equal hazards and into effects on either side. A p-value alone would hide the range of effects still compatible with the data; the interval makes that uncertainty visible.

It also demonstrates that different statistical summaries can answer different questions. The Cox analysis uses time-to-event information and reports a hazard ratio, while the unadjusted recalculation compares event proportions using a risk difference. Their p-values are close, but the effect measures are not interchangeable. A clear statistical explanation should identify the estimand rather than treating every comparison as the same result.

The composite endpoint is another important issue. Combining thrombotic events, hospitalization, and death creates one primary outcome, but the overall estimate cannot identify which components contributed to it. Without component-specific results, readers cannot determine whether the composite pattern was uniform across its parts. This limitation is especially relevant when a result is summarized as a single treatment contrast.

Finally, the record leaves gaps about missing data, multiplicity, interim analyses, and the original sample-size rationale. These are not grounds for assuming a particular flaw; they are limits on what can be evaluated from the public record. Statistical interpretation depends not only on a test result but also on knowing how the analysis was planned and implemented.

19. 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 endpoint combines multiple event types, and component-specific results are not reported in the registry record. As a result, the overall comparison cannot show whether findings differed for thrombotic events, hospitalization, or mortality, or which components contributed most to the composite.

The primary event counts are limited, and the reported confidence interval is broad. This constrains precision and leaves a wide range of relative effects compatible with the data. The registry does not report a threshold for a clinically important effect, so the clinical importance of values within that range cannot be assessed from the record alone.

The study is listed as terminated, but the reason for termination is not reported. Missing-data methods, follow-up completeness, censoring details, interim analyses, and stopping rules are also not reported. These omissions prevent a full assessment of whether and how these factors affected the analysis.

The registry gives no original sample-size justification or planned effect assumption. The displayed planning illustrations are based on the observed effect and are not a record of the trial’s design targets. The available record also does not describe details of standard of care, treatment adherence, or the distribution of follow-up across participants.

Secondary results are incomplete: results for the listed secondary efficacy outcome are not reported, and no multiplicity adjustment is described. The safety summaries use different denominators from the primary endpoint, with no explanation in the registry record. These limits mean that the public information supports a bounded interpretation of the posted primary result, rather than a complete assessment of efficacy, safety, or study conduct.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Rivaroxaban to Reduce the Risk of Major Venous and Arterial Thrombotic Events, Hospitalization and Death in Medically Ill Outpatients With Acute, Symptomatic Coronavirus Disease 2019 (COVID-19) Infection — NCT04508023.
• Registry record last updated 2023-07-18; status last verified 2023-07.
• Results first posted 2023-07-18.
• 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.

23. Record Summary

NCT04508023 is a randomized, double-masked, parallel-group Phase 3 study of rivaroxaban versus matching placebo, both alongside standard of care, in medically ill outpatients with acute, symptomatic COVID-19. The registry lists an enrollment of 1284, a start date of 2020-08-13, a primary completion date of 2022-06-01, and status as terminated.

The primary endpoint was time to first occurrence of a composite of thrombotic events, all-cause hospitalization, and all-cause mortality through Day 35. The posted event counts were 22 of 641 with rivaroxaban and 19 of 643 with placebo. The reported hazard ratio was 1.16, with a 95% confidence interval from 0.63 to 2.15 and p = 0.626. The estimate is imprecise and does not establish a clear difference between groups.

The record does not report the reason for termination, original sample-size assumptions, missing-data methods, or a multiplicity procedure for secondary outcomes. Secondary and safety results provide limited additional context.