Clinical Trial Evaluating the Efficacy and Safety of Favipiravir in Moderate to Severe COVID-19 Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial Evaluating the Efficacy and Safety of Favipiravir in Moderate to Severe COVID-19 Patients (NCT04529499), a randomized phase 3 study. The primary outcome is Primary Efficacy Endpoint: Time to Resolution of Hypoxia (Stage I).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group trial sponsored by Dr. Reddy's Laboratories Limited. The registry lists an enrollment of 353 and describes the trial as multi-center, double-blind, and placebo-controlled. It began on 2020-08-22, had a primary completion date of 2021-01-22, and is listed as terminated. The reason for termination is not reported in the registry record.

The intervention was favipiravir plus supportive care, compared with placebo plus supportive care. The favipiravir arm description specifies twice-daily tablets, 1,800 mg twice daily on Day 1, followed by 800 mg twice daily for up to 9 days. The placebo arm description gives a tablet schedule for up to the same period. These regimen details describe the registered protocol; they do not establish how consistently treatment was received.

The registry describes two parts: Stage I, the main study, and Stage II, extended follow-up. The primary endpoint and the listed mortality outcome are identified as Stage I outcomes. The primary analysis population included randomized patients with a baseline clinical status score >4 on the WHO 10-point ordinal scale. Primary-endpoint arm counts are 157 and 158, while the secondary mortality outcome and safety summaries have different denominators. Those populations should not be treated as interchangeable.

The registry record does not report the original sample-size justification, the intended allocation ratio, details of randomization implementation, or a reason for stopping the trial. Those omissions limit assessment of how the planned design relates to the analyses posted.

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:

Analysis population for the primary outcome, as defined in the registry: Analysis population (Intent-to-treat) was all randomized patients who had a clinical status score \>4 on WHO 10-point ordinal scale at baseline

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 Primary Efficacy Endpoint: Time to Resolution of Hypoxia (Stage I), measured over 1-28 days.

The primary endpoint was time to resolution of hypoxia during the 1-28 day timeframe. Resolution required reaching a score of 4 or lower on the WHO 10-point ordinal clinical-status scale, including maintaining blood oxygen saturation of ≥ 95% at rest on room air at sea level when assessed over 24 hours. The endpoint therefore combines a clinical-status threshold with a specified oxygenation condition rather than recording oxygen saturation alone.

Time-to-event outcomes are useful when both whether an event occurs and when it occurs matter. They can account for the timing of resolution and, depending on the analysis, for participants whose event time is not observed within the follow-up period. The registry identifies the endpoint as a median time and reports medians with inter-quartile ranges for the two arms. It also reports a hazard ratio from a Cox proportional hazards analysis.

The registry record does not describe the handling of participants who did not resolve hypoxia during the observed period, or give additional detail about censoring. Such details matter when interpreting time-to-event analyses. The endpoint definition also limits the inference: it concerns the registered resolution criterion over the specified period, not every aspect of recovery or later health.

7. Results Posted in the Registry

• Favipiravir + Supportive Care vs Placebo + Supportive Care: hazard ratio 0.99 (95% CI 0.77–1.28) (as reported in the registry).

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.

Percentage of Patients Dying (All Cause (Stage I)

• 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:
  • Favipiravir + Supportive Care: 6.3% (11/175) versus 3.9% (7/178) on control; risk difference 2.4 percentage points (95% CI -2.2 to 6.9), risk ratio 1.60 (0.63–4.03); unadjusted two-proportion z-test p = 0.315.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Favipiravir + Supportive Care and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: all-cause mortality during the 1-28 day period. Its group comparison does not provide clear statistical evidence of a difference, and the uncertainty around the unadjusted estimate includes the null. This is broadly a non-definitive result rather than confirmation of either benefit or harm. The primary endpoint measures time to resolution of hypoxia, while mortality is a different outcome; the two should not be treated as interchangeable measures of the same event.

Secondary outcomes generally carry less weight than a prespecified primary outcome because they may be numerous, exploratory, or less central to the trial's main question. When several outcomes are tested, the chance of at least one apparently unusual result can increase unless multiplicity is addressed. The registry record does not report a multiplicity adjustment or describe a hierarchy for interpreting secondary outcomes.

The limited set of posted secondary results also constrains conclusions about the broader pattern of outcomes. The record does not provide a complete account of all outcomes originally planned, whether other results were collected, or how secondary analyses were selected for posting. Thus, the secondary result can add context but should not override the primary analysis or be treated as an independent confirmation of it.

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

• Percentage of Patients Dying (All Cause (Stage I)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents both a summary of time to resolution and a comparison of the groups. Each method answers a somewhat different statistical question. Their interpretation also depends on assumptions and reporting details that are not fully available in the registry record.

What does a median time describe?

A median is the point at which half of the observations are at or below the value and half are at or above it, subject to how the analysis handles censored observations. For a time-to-event outcome, the median summarizes when the event has occurred for the middle of the estimated distribution. The registry reports 7 days for favipiravir plus supportive care and 8 days for placebo plus supportive care. These summaries do not show the full distribution, and a comparison of the two medians alone is not the same as a formal test of the time-to-event curves.

The inter-quartile range describes the span between the lower and upper quartiles of the distribution. The reported ranges are 4 to 11 days and 5 to 12 days. They convey variation in observed or estimated event times, but do not quantify uncertainty in the difference between groups. Nor do they describe every individual time to resolution.

What does the log-rank test assess?

In general, the log-rank test compares time-to-event experience across groups over follow-up. It uses information about event timing and is commonly used when observations may be censored. Its p-value, reported as 0.67, indicates how compatible the test statistic is with the null hypothesis under the test's assumptions; it is not the probability that the null hypothesis is true. The registry record does not provide the detailed censoring rules or a fuller account of how this test was implemented.

How should the hazard ratio be read?

The registry reports a Cox proportional hazards estimate of 0.991, with a 95% confidence interval of 0.767 to 1.280. In general, a hazard ratio compares the instantaneous event rates between groups over follow-up, conditional on the model. A value of 1 represents no relative difference in those rates. Interpreting which arm has a higher event rate depends on the event coding and the order of groups in the model. Because the registry record does not spell out that coding, the numerical direction should not be converted into a claim that one arm reached resolution sooner.

The Cox model also relies on assumptions, including proportional hazards: broadly, that the relative hazards are sufficiently stable over time for a single hazard ratio to be informative. The registry record does not report an assessment of this assumption. A single hazard ratio can be an incomplete summary if relative event rates change over time.

Why does over-dispersion matter in general?

Over-dispersion occurs when data vary more than a statistical model expects. In general, ignoring it can make standard errors too small and confidence intervals too narrow, giving an overly confident impression of precision. It is not a reported issue in this trial, and the registry record does not describe a model for over-dispersion. The concept is relevant to methods that model counts or rates, but it should not be presumed to affect these reported analyses.

How does the mortality comparison differ?

The mortality outcome is binary: each participant is counted as having died or not having died during the stated timeframe. The sponsor's posted analysis uses a Fisher exact test, with p = 0.34. A Fisher exact test evaluates the association between group and the binary outcome using the observed counts, without relying on a large-sample approximation in the same way as some other tests. The re-calculated risk difference is an unadjusted comparison based on posted summary counts; its confidence interval includes zero, so the data remain compatible with no difference as well as with a range of possible differences.

The re-calculated p-value is 0.315, which is not identical to the reported 0.34. These values come from different analyses, and p-values can differ with the method used. The registry record does not describe adjustment variables for the sponsor's mortality analysis. The re-calculation is not a replacement for an analysis based on participant-level data.

In general, an unadjusted comparison does not account for covariates or design features beyond the grouping used in the calculation. A posted summary-statistic re-calculation can therefore be used as a descriptive check, not as evidence that the original analysis was reproduced in full. The sponsor's reported analysis remains an important part of the record, and method differences should be kept visible rather than collapsed into one result.

11. Confidence Intervals and Precision

The confidence interval for the primary hazard ratio is 0.767 to 1.280 at the 95% level. In general, a confidence interval expresses the range of estimates compatible with the data and method under repeated-sampling assumptions. It is not a guarantee that the true value lies in the interval, nor does it measure the probability that a particular treatment effect is correct.

This interval includes 1, the null value for a hazard ratio. It is compatible with relative hazards below or above that value, so the estimate does not precisely distinguish between no relative difference and effects in either direction. The registry's log-rank p-value of 0.67 likewise does not supply evidence of a clear group difference. Neither result proves equivalence or establishes that any potential difference is clinically unimportant; the record does not give an equivalence margin.

For the secondary mortality comparison, the re-calculated risk-difference interval extends across zero. In general, zero is the null value for an absolute difference in risks. The interval therefore includes no difference as well as possible differences in either direction. The precision is limited, and the estimate should be interpreted alongside the posted Fisher exact test rather than as a definitive result.

The range of uncertainty matters as much as the point estimate. A p-value alone does not communicate the scale of effects compatible with the data, while a confidence interval does not remove uncertainty or resolve questions about bias, endpoint definition, or analysis assumptions. The registry record does not provide all the details needed to assess those issues fully.

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 trial's original sample-size design. For the time-to-event endpoint, the figures are total events required. For the other outcome, they are participants per arm. They should not be read as the actual number of events or participants observed in the trial.

The illustration assumes 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. The registry record does not report the trial's own original design assumptions or sample-size justification.

The 80% power column describes the planning number that would give an 80% chance of detecting the specified effect under those assumptions if that effect were the true effect. The 90% power column uses a higher target chance of detection. Neither is a guarantee that a study will detect an effect, and both depend on the assumptions being suitable. This is not observed power.

The rows for 100%, 75%, and 50% of the observed effect show how the planning requirements change when the effect to detect is made smaller. Smaller effects generally require more events or participants to distinguish them from chance variation. The figures are planning illustrations only; they do not indicate the trial's actual power or establish whether its original design was adequate.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.991, so ln(HR) = -0.0090.
2. d = 4 × (1.96 + 0.842)² / [ln(0.991)]² = 384,113.2, rounded up to 384,114 events in total 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
hr <- 0.991                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(4529499)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 384,114 (80% power), 514,219 (90% power)
 75% of observed effect: events = 682,868 (80% power), 914,167 (90% power)
 50% of observed effect: events = 1,536,453 (80% power), 2,056,875 (90% power)
Simulated power with 384,114 events: 0.795 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 522,025 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 353 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 0.23013698630137          # control-arm median, months (converted from the posted unit)
hr          <- 0.991          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
       Analysis               Value Efficacy
      IA 1: 33%                   Z   3.7103
      N: 181240         p (1-sided)   0.0001
 Events: 173430        ~HR at bound   0.9823
       Month: 8    P(Cross) if HR=1   0.0001
                P(Cross) if HR=0.99   0.0338
      IA 2: 67%                   Z   2.5114
      N: 355248         p (1-sided)   0.0060
 Events: 346860        ~HR at bound   0.9915
      Month: 16    P(Cross) if HR=1   0.0060
                P(Cross) if HR=0.99   0.5603
          Final                   Z   1.9930
      N: 522026         p (1-sided)   0.0231
 Events: 520290        ~HR at bound   0.9945
      Month: 60    P(Cross) if HR=1   0.0250
                P(Cross) if HR=0.99   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The primary outcome results include the sponsor's reported log-rank p-value of 0.67 and Cox proportional hazards estimate of 0.991 with a 95% confidence interval of 0.767 to 1.280. The registry record does not provide a separate re-calculated primary hazard ratio. These reported analyses therefore anchor interpretation of the primary time-to-event result.

For the mortality outcome, the sponsor reports a Fisher exact test p-value of 0.34. The unadjusted re-calculation from posted summary statistics gives p = 0.315. The small difference between these p-values reflects that the re-calculation is not the same analysis as the sponsor's posted test; it should not be treated as a correction to it. The registry record marks no discrepancy between the analyses.

A re-calculation based on summary counts is limited to those counts and the chosen unadjusted method. It cannot reproduce analyses that may depend on participant-level information or additional handling details absent from the registry record. Both the reported analysis and the re-calculation are consistent with substantial uncertainty about the mortality comparison, but the sponsor's analysis is the trial's reported result.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or analyses are tested. In general, conducting many tests increases the chance that at least one result will appear statistically unusual by chance. Researchers may address this with a prespecified hierarchy, adjusted significance thresholds, or other procedures, but the registry record does not report whether such a plan was used.

The record identifies a primary endpoint and one posted secondary outcome. It also describes two study stages, but does not explain whether outcome testing was planned across stages or whether there were other planned analyses. The multiplicity strategy, if any, is not reported in the registry record. Therefore the posted p-values should be interpreted as reported tests, not as evidence that all possible testing has been accounted for.

Missing-data handling is also not reported in the registry record. For a time-to-event outcome, censoring and incomplete follow-up can affect which information contributes to an estimate. For a binary mortality outcome, the handling of participants whose status is unknown would matter. The registry record does not state how missing observations were treated, whether imputation was used, or what sensitivity analyses were conducted.

The primary analysis population is described as randomized patients with baseline clinical status score >4, but further detail about exclusions or analysis-set construction is not reported. The registry record also does not give a detailed statistical analysis plan, an account of interim analyses, or a full description of prespecification. These are limitations on evaluating whether the reported methods were chosen before results were known; they do not establish that particular procedures were or were not performed.

17. 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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute respiratory distress syndrome (4.2%), respiratory failure (4.2%), acute respiratory failure (0.6%), acute kidney injury (0.6%), covid-19 pneumonia (0.6%).

The safety summary reports serious adverse events among 19 of 168 participants in the favipiravir plus supportive care group and 14 of 166 in the placebo plus supportive care group. Other adverse events are reported for 18 of 168 and 11 of 166, respectively. The safety summary also lists 14 deaths in the favipiravir group and 11 in the placebo group. These are descriptive counts with their stated denominators; the registry does not provide a statistical comparison for these safety summaries.

Acute Respiratory Distress Syndrome and Respiratory Failure are each listed at 4.2% among the top serious adverse event terms. Other listed terms are reported at 0.6% each. These figures describe the registered event terms and should not be interpreted as evidence that an event was caused by a treatment. The record does not provide enough information in these summaries to assess timing, severity patterns, relatedness, or differences in exposure.

The denominators in the safety summary differ from those for the efficacy outcomes. The counts should therefore be read within their own reported safety population, not combined with or substituted for the efficacy analysis populations. Adverse-event counts alone do not establish comparative safety.

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

The registry results describe a randomized comparison of favipiravir added to supportive care with placebo plus supportive care in patients with moderate to severe COVID-19. For the primary endpoint, the reported medians were 7 days and 8 days, and the reported hazard ratio was 0.991 with a 95% confidence interval of 0.767 to 1.280. The log-rank p-value was 0.67. These results do not provide clear statistical evidence of a difference in time to resolution of hypoxia.

That interpretation is not the same as proving that the treatments have identical effects. The confidence interval remains compatible with a range of relative hazard values, and the registry does not give an equivalence or non-inferiority margin. A non-significant result also does not show that a clinically important effect is impossible. The posted evidence is uncertain, and the direction of the hazard ratio cannot be translated into faster or slower resolution without the event coding.

The secondary mortality result is also inconclusive. It concerns a different endpoint and should not be used as a substitute for the primary result. The registry's safety counts are descriptive and do not by themselves establish a causal relationship between treatment and any reported event.

These findings apply to the registered endpoints, populations, and follow-up period. They do not answer every question about recovery, longer-term outcomes, other patient groups, or other treatment settings. The trial is listed as terminated, but the reason is not reported in the registry record. Interpretation is further limited by missing details about the analysis plan, missing-data handling, and the original sample-size justification.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition, estimand, analysis method, and uncertainty rather than from a single point estimate. The primary outcome is a time-to-event measure with a specific clinical-status and oxygenation threshold. The median summaries and the hazard ratio describe different features of the data, while the log-rank test supplies a separate comparison. They provide context for one another but are not interchangeable.

The reported hazard ratio is close to the null value, but its confidence interval spans values on both sides of the null. That distinction shows why a point estimate alone is not a measure of precision. The result does not establish equivalence, and the registry record gives no equivalence margin. Conversely, the absence of clear statistical evidence does not demonstrate a treatment difference.

The record also highlights the importance of distinguishing outcome populations. The primary analysis, mortality result, and safety summaries have different denominators. Without keeping those populations separate, it would be easy to misread counts as directly comparable when they are not.

Finally, registry reporting details shape how much can be inferred. The original sample-size justification, multiplicity strategy, missing-data methods, and reason for termination are not reported in the registry record. These gaps matter for assessing precision and robustness. Clear reporting of such details helps readers distinguish a result that is genuinely precise from one that remains uncertain.

20. Limitations

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

Several limitations specific to this record constrain interpretation. The trial is listed as terminated, but the reason for termination is not reported in the registry record. Without that context, the relationship between the planned study and the posted results cannot be fully assessed. The registry record also does not report the original sample-size justification or the assumptions used to plan enrollment.

The primary endpoint is defined in detail, but the registry does not describe the censoring rules, missing-data handling, or assessment of the proportional hazards assumption. These details can influence time-to-event estimates. The event coding for the hazard ratio is also not stated, limiting interpretation of its direction.

The record gives the primary analysis population and outcome-specific denominators, but does not fully explain differences among the efficacy and safety populations. The mortality outcome has a reported sponsor test and an unadjusted re-calculation from summary statistics; the latter cannot substitute for analyses using participant-level data. Multiplicity procedures and the full set of originally planned secondary analyses are not reported.

Masking is described as quadruple, but the identities of the masked groups are not specified. The record does not provide detail on adherence, treatment discontinuation, protocol deviations, or site-level variation. These omissions do not establish that a problem occurred, but they limit independent assessment of implementation and analysis. Findings should therefore be kept within the specific outcomes and follow-up described.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Clinical Trial Evaluating the Efficacy and Safety of Favipiravir in Moderate to Severe COVID-19 Patients — NCT04529499.
• Registry record last updated 2022-03-21; status last verified 2022-03.
• Results first posted 2022-03-21.
• 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.

24. Record Summary

NCT04529499 is a terminated Phase 3, randomized, quadruple-masked, parallel-group trial of favipiravir plus supportive care versus placebo plus supportive care in moderate to severe COVID-19. The registry lists enrollment of 353 and identifies time to resolution of hypoxia during 1-28 days as the primary efficacy endpoint.

The reported primary analyses include a median time of 7 days versus 8 days, a Cox hazard ratio of 0.991 with a 95% confidence interval of 0.767 to 1.280, and a log-rank p-value of 0.67. The posted mortality comparison is not conclusive. Safety summaries are descriptive and use different denominators from the efficacy outcomes.

The registry record does not report the reason for termination, the original sample-size justification, or several important analysis details, including missing-data and multiplicity methods.