High-Dose Versus Standard-Dose Oseltamivir to Treat Severe Influenza and Avian Influenza: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for High-Dose Versus Standard-Dose Oseltamivir to Treat Severe Influenza and Avian Influenza (NCT00298233), a randomized phase 2 study. The primary outcome is Proportion of All Participants Negative for Viral RNA on Day 5.

2. Clinical Question

3. Trial Design

The registry identifies NCT00298233 as a phase II, randomized, triple-masked, parallel-group trial. It lists enrollment of 326 and a completed status. The sponsor was the National Institute of Allergy and Infectious Diseases (NIAID). The record gives a start date of 2006-02 and a primary completion date of 2010-01.

The study compared double-dose, also called high-dose, oseltamivir with standard-dose oseltamivir. The arm descriptions distinguish adult participants, aged 15 years or older, from child participants younger than 15 years. The adult standard-dose regimen is described as 75 mg twice daily orally, and the high-dose regimen as 150 mg twice daily orally. Equivalent doses adjusted for age, weight, and kidney function are also allowed in the descriptions. Both regimens are specified for 5 to 10 days.

The trial description focuses on people hospitalized with severe human influenza or avian influenza. The primary outcome population is narrower in its wording: all randomized patients with influenza proven by RT-PCR. The registry lists the primary endpoint as the proportion of participants negative for viral RNA on day 5, with secondary outcomes including clinical failure on day 5, in-hospital mortality, and time receiving oxygen, in intensive care, and on ventilation.

The record does not report the allocation sequence method, concealment procedures, or which parties were masked. It also does not report the original sample-size justification or the trial's planned statistical analysis in enough detail to reconstruct them. Those omissions limit assessment of design choices beyond the features explicitly listed in the registry.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All randomized patients with RT-PCR proven influenza.

5. Baseline Characteristics

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

Population: All participants that were randomized

6. Primary Endpoint

The registry lists the primary outcome as Proportion of All Participants Negative for Viral RNA on Day 5, measured over After 5 days of treatment.

The primary endpoint is the proportion of participants with no detectable viral RNA after 5 days of treatment. The registry defines a negative result using reverse transcriptase-polymerase chain reaction (RT-PCR) on a combined nasal and throat swab sample. The stated population is all randomized patients with RT-PCR proven influenza.

This is a binary endpoint: each participant is classified according to whether viral RNA was detected at the specified assessment. The outcome counts therefore represent participants meeting the negative-test criterion, rather than a continuous measure of viral quantity. Comparing proportions between dose groups gives a direct estimate of how frequently the endpoint occurred in each group.

As a general statistical point, a laboratory endpoint can provide a defined, reproducible measure at a specified time. It does not, by itself, describe every aspect of a participant's clinical course. That distinction matters because the registry separately lists clinical failure, mortality, and measures of oxygen use, intensive care, and ventilation as secondary outcomes. The day-5 viral RNA result should therefore be interpreted as the result for this particular test-based endpoint, not as a substitute for all clinical outcomes.

The registry does not report the assay's detection threshold or further operational details for classifying missing or indeterminate test results. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Double Dose Oseltamivir: 72.3% (115/159) versus 68.2% (105/154) on control; risk difference 4.1 percentage points (95% CI -6.0 to 14.3), risk ratio 1.06 (0.92–1.23); unadjusted two-proportion z-test p = 0.422.

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.

Participants Meeting Criteria for Day 5 Clinical Failure

• 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:
  • Double Dose Oseltamivir: 9.9% (16/161) versus 12.7% (20/158) on control; risk difference -2.7 percentage points (95% CI -9.7 to 4.2), risk ratio 0.79 (0.42–1.46); unadjusted two-proportion z-test p = 0.443.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double Dose Oseltamivir and the control. The interval gives the range of effects that remain compatible with the data.

In-hospital Mortality Rates

• 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:
  • Double Dose Oseltamivir: 7.3% (12/165) versus 5.6% (9/161) on control; risk difference 1.7 percentage points (95% CI -3.6 to 7.0), risk ratio 1.30 (0.56–3.00); unadjusted two-proportion z-test p = 0.536.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double Dose Oseltamivir and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes with numerical comparisons include day-5 clinical failure and in-hospital mortality. Their recalculated point estimates do not move in the same direction: the estimate for clinical failure is lower in the double-dose group, while the estimate for mortality is higher in that group. Both comparisons are uncertain, and their intervals include no difference. This mixed pattern does not provide a consistent secondary signal that clearly reinforces the primary endpoint result.

The registry also lists time receiving oxygen, time in intensive care, and time on ventilation. Numerical findings for these outcomes are not reported in the registry record, so their directions, sizes, and precision cannot be assessed. The record identifies additional outcome measures, but listing an outcome is not equivalent to posting an estimate for it.

Secondary endpoints can help describe different aspects of participants' outcomes, but they generally provide less decisive evidence when many outcomes are examined without a reported multiplicity plan. Each additional comparison creates another opportunity for a result to appear noteworthy by chance. The registry does not report whether secondary comparisons were adjusted for multiplicity, prespecified in a hierarchy, or treated as exploratory. Their findings should therefore be interpreted cautiously and in context of the primary endpoint rather than as independent proof.

The secondary results neither erase nor resolve the uncertainty in the primary comparison. The available numerical results are limited, point in different directions, and do not establish a uniform effect across outcomes. Missing numerical results for the other listed measures further constrain an overall assessment of the secondary outcome pattern.

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

• Participants Meeting Criteria for Day 5 Clinical Failure
• In-hospital Mortality Rates
• Median Time (Days) Receipt of Oxygen
• Median Time (Days) in ICU
• Median Time (Days) on Ventilation

9. Statistical Interpretation

10. Statistical Methods Explained

The posted recalculations compare the proportion meeting a binary outcome in the double-dose and standard-dose groups. For the primary endpoint, the event is a negative viral RNA test on day 5. A risk is the proportion of participants meeting that event criterion in a group. The risk difference subtracts the standard-dose proportion from the double-dose proportion, so a positive estimate indicates a higher observed proportion in the double-dose group.

What does the risk difference convey?

The risk difference stays on the scale of proportions and describes the absolute separation between the observed group risks. It is useful because it expresses the comparison in terms of how much the event proportion differs, rather than as a relative change. Its interpretation depends on which event is being counted: a positive difference favors the group with more of that event only if more of that event is the desired direction. For viral RNA negativity, more participants meeting the endpoint means more negative tests; for an adverse outcome such as clinical failure, more events have a different meaning.

For the primary endpoint, the recalculated risk difference is 0.042, with an interval from -0.060 to 0.143. The group proportions and counts are also posted, allowing the event definition and denominators to be read alongside the contrast. The recalculation is unadjusted: it uses the posted summary counts and does not account for covariates or other features of the analysis.

How should the interval be read?

A confidence interval represents uncertainty around an estimated effect under the assumptions of the method used. In general, a wider interval indicates less precision, while an interval that includes the no-difference value is compatible with no group difference as well as effects in either direction. The primary interval crosses zero, so the posted estimate does not narrowly distinguish a positive difference from a negative one. The confidence level for the posted recalculated intervals is not reported in the registry record.

A p-value addresses how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The recalculated unadjusted p-value for the primary comparison is 0.422; the registry reports p = 0.42 for its own analysis. The registry does not report a detailed statistical analysis plan that would identify every model specification or decision rule.

Why can the sponsor result differ in form?

The registry lists conditional univariate logistic regression for the primary comparison and gives a p-value, but no effect estimate or interval from that analysis. Logistic regression models the odds of a binary outcome, while the displayed recalculation is a risk difference from summary proportions. These are different statistical summaries and can incorporate different assumptions. The record does not report enough detail to reconstruct the sponsor's model. The registry's own analysis is therefore the primary reported inferential result; the simple recalculation is a complementary description, not a replacement.

Why do event counts and denominators matter?

A proportion must be interpreted with both its event count and its denominator. The primary endpoint lists 115 events among 159 in the double-dose arm and 105 among 154 in the standard-dose arm. Those denominators are not the same as the enrollment figure, and other outcomes use their own denominators. The registry does not explain the reasons for this variation or report how missing data were handled. A difference in analyzed denominators may reflect outcome availability or analysis-population definitions, but those explanations cannot be established from the record.

For sparse outcomes, such as mortality or serious adverse events, estimates may be especially imprecise because few events are recorded. As a general statistical principle, limited event information can make intervals broad and estimates sensitive to small changes in counts. The posted intervals for the secondary binary outcomes reflect uncertainty and should be read alongside the actual event counts.

What is the role of over-dispersion?

Over-dispersion refers generally to more variability in data than a chosen model expects. It is most relevant to models for counts or clustered observations, where treating observations as more independent or less variable than they are can lead to overly narrow uncertainty estimates. The primary outcome is recorded as a binary participant count, and the registry does not report an over-dispersion adjustment. It would not be appropriate to assume that such an adjustment was used.

More generally, the method and its assumptions determine what an interval and p-value mean. Randomization is listed, but details of stratification, covariate adjustment, missing-data handling, and multiplicity control are not reported in the registry record. These omissions limit independent reproduction of the sponsor's full analysis and should temper claims that go beyond the posted comparisons.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.042, with a posted interval from -0.060 to 0.143. The lower end is negative and the upper end is positive, so the range includes both a possible lower proportion in the double-dose group and a possible higher proportion. The interval also includes zero, the value corresponding to no risk difference. The estimate therefore has meaningful uncertainty in both direction and size.

The point estimate is only one summary of the comparison. It locates the observed risk difference, while the interval communicates how much uncertainty surrounds that estimate under the calculation's assumptions. A broad range relative to the point estimate means the observed data do not pin down the underlying difference closely. The confidence level for the recalculated interval is not reported in the registry record, so it should not be labeled with an assumed level.

The sponsor's analysis reports p = 0.42 but does not post an effect estimate or interval for that model. A p-value alone does not show the range of effect sizes compatible with the data, and it cannot replace an interval for judging precision. The unadjusted recalculation supplies an interval based on the summary counts, but it is not the same analysis as the sponsor's conditional logistic regression.

The secondary binary comparisons also have uncertainty, and their event counts are limited relative to their denominators. The estimates should not be treated as precise merely because a single point value is available. The registry does not report numerical results for all listed secondary outcomes, so precision cannot be evaluated for those measures.

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 are for participants per arm for 80% power and participants per arm for 90% power. The record's assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. These are planning assumptions for illustrations; the trial's original design assumptions and sample-size justification are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 1,908 participants per arm for 80% power and 2,554 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,427 participants per arm for 80% power and 4,587 participants per arm for 90% power. Planning for 50% of the observed effect gives 7,785 participants per arm for 80% power and 10,422 participants per arm for 90% power. The same planning framework is used for the posted binary secondary outcomes.

In plain terms, a power column describes the chance, under the assumed effect and analysis conditions, of detecting an effect at the chosen significance level if that effect is truly present. A higher target power generally requires more participants. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. These illustrations are not observed power and do not indicate the probability that the trial's result is correct.

The sample-size assumptions are not a substitute for the original protocol's design rationale. In particular, using the observed effect for a planning illustration does not establish that the trial was designed to detect that effect.

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 = 0.682; treatment proportion p₁ = 0.723; average p̄ = 0.703.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6465 = 1.2671.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6458 = 0.5435.
4. n = (1.2671 + 0.5435)² / (0.0415)² = 1,908.0, rounded up to 1,908 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 <- 0.681818181818182                          # control proportion
p1 <- 0.723270440251572                          # 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(298233)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,908 (80% power), 2,554 (90% power)
 75% of observed effect: n per arm = 3,427 (80% power), 4,587 (90% power)
 50% of observed effect: n per arm = 7,785 (80% power), 10,422 (90% power)
power.prop.test: 1908 
Simulated power at n = 1,908 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 own primary analysis is listed as conditional univariate logistic regression and reports p = 0.42. It does not provide an effect estimate or interval for that model. The recalculation from the posted primary counts gives an unadjusted risk difference of 0.042, an interval from -0.060 to 0.143, and an unadjusted p-value of 0.422.

These results are similar in their broad statistical reading: neither p-value indicates strong evidence against a no-difference null, and the recalculated interval includes zero. However, they are not interchangeable. The sponsor's listed method is logistic regression, whereas the recalculation compares the two observed proportions directly on the risk-difference scale. The registry does not provide sufficient model details to reproduce the sponsor's analysis or to explain the exact relationship between the two p-values.

The record does not flag a discrepancy between the sponsor result and the recalculation. The sponsor's analysis remains the reported trial analysis; the recalculation is a simple, unadjusted supplement based on summary statistics. It should not be interpreted as a correction to the sponsor's result or as a more authoritative model-based estimate.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and multiple secondary outcomes. It does not report whether the analysis plan controlled the family-wise error rate, used another multiplicity adjustment, or specified a hierarchy for interpreting secondary tests. When several outcomes are tested, the chance of at least one apparently notable result can increase. As a general statistical principle, unadjusted secondary p-values should be treated as exploratory unless the analysis plan justifies a different interpretation.

The primary population is described as all randomized patients with RT-PCR proven influenza. The record does not fully describe the analysis population used for every outcome, nor does it explain why the denominators vary across the primary and secondary analyses. It also does not report the number of missing measurements or the methods used to handle missing endpoint data. These details are important because excluding participants with unavailable outcomes can affect both the estimate and its generalizability.

The record does not report imputation methods, sensitivity analyses for missing data, or rules for handling indeterminate test results. It also does not give a detailed protocol-level statistical plan or specify whether any interim analyses were planned or conducted. These items are not reported in the registry record and should not be inferred from the posted results.

Randomized allocation is reported, but the registry does not describe the sequence-generation or allocation-concealment procedures. Triple masking is listed, but the record does not identify which groups of people were masked. These gaps do not establish that the procedures were inadequate; they limit what can be verified from the registry entry.

16. Safety Results

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

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: septic shock (0.6%).

The adverse-event record lists one serious adverse event in the double-dose group and none in the standard-dose group. The serious-event denominators are 165 and 161, respectively. Septic shock is listed as the top serious term, at 0.6%. The record also lists other adverse events for 37 participants in the double-dose group and 38 in the standard-dose group, using denominators of 165 and 161.

These counts should be read as registry-reported adverse-event summaries, not as a complete comparison of every possible safety outcome. The record does not provide event-level details, severity grading beyond the serious-event classification, attribution to treatment, or follow-up beyond the listed treatment period. Deaths are not reported in the adverse-event group fields. In-hospital mortality is separately listed as a secondary outcome, with its own posted analysis.

Small numbers of serious events make comparative safety estimates especially uncertain. The registry counts alone do not establish whether a treatment caused an event or whether the groups differ meaningfully in safety. They describe what was recorded in the posted adverse-event fields.

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

The primary result describes the proportion of randomized patients with RT-PCR proven influenza who had no detectable viral RNA on day 5. The observed proportion was higher in the double-dose group, and the recalculated risk difference was positive. Its interval includes zero and extends in both directions, leaving substantial uncertainty about the size and direction of the underlying difference.

This result does not establish that high-dose oseltamivir is superior, equivalent, or inferior to standard-dose oseltamivir. A result that does not distinguish clearly from no difference is not proof that the treatments have identical effects. The posted data also do not establish that a difference in viral RNA negativity translates into a difference in clinical outcomes.

The registry separately lists clinical failure, in-hospital mortality, oxygen use, intensive care, and ventilation outcomes. Numerical results are available for some of these, but not all. The available secondary point estimates do not all point in the same direction, and their intervals are uncertain. The unreported outcomes cannot be used to support either a favorable or unfavorable interpretation.

Interpretation is also limited by the absence of a detailed account of missing data, the reasons for different analysis denominators, and the original statistical plan. The record describes a phase II trial and a particular hospitalized population; it does not establish how the findings apply beyond that population. These results are statistical evidence about the outcomes and groups recorded, not medical advice or a comprehensive assessment of treatment choice.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition matters. A test-based outcome such as day-5 viral RNA negativity is distinct from clinical failure, mortality, or time receiving supportive care. Keeping those outcomes separate prevents a laboratory result from being interpreted as if it answered every clinical question.

It also demonstrates the value of reading an effect estimate with its uncertainty. The primary point estimate is positive, but its interval includes zero and ranges in both directions. A single observed proportion or p-value cannot convey that uncertainty on its own. The reported sponsor analysis and unadjusted recalculation also use different statistical approaches, so their results should be understood in relation to the method that generated them.

The record offers a further lesson about secondary endpoints and incomplete reporting. Some secondary outcomes have numerical comparisons, while others are listed without results. Without a reported multiplicity strategy, secondary findings warrant caution. Without missing-data details and explanations for denominator variation, readers cannot fully assess how the analyzed groups relate to the intended population.

Finally, planning illustrations based on observed effects are not evidence of the trial's original design adequacy. They show how assumed effect size and target power influence participant requirements under stated planning conditions. The registry's own sample-size rationale is not reported. Together, these issues show why statistical interpretation depends not only on the point estimate, but also on endpoint choice, precision, analysis methods, and the completeness of the record.

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 registry does not report the original sample-size calculation or the assumptions used to plan enrollment. The posted planning illustrations are based on the observed effect and should not be treated as a reconstruction of the original design. The statistical analysis plan is also not reported in enough detail to identify all model specifications, decision rules, or planned sensitivity analyses.

Although the trial is described as randomized and triple-masked, the registry does not state how the allocation sequence was generated or concealed, or identify who was masked. It does not report whether the randomization or analysis accounted for the adult and child cohorts, nor does it give a subgroup analysis by age or influenza type. Such analyses should not be presumed.

The primary and secondary outcome denominators differ, and the registry does not explain the differences. Missing-data counts and handling methods are not reported, as are assay thresholds or rules for indeterminate results. This prevents a fuller assessment of outcome completeness and the relationship between the analyzed populations and all randomized participants.

Numerical results are not reported for every listed secondary endpoint, and multiplicity handling is not described. The sponsor's primary analysis reports a p-value but no effect estimate or interval, limiting direct assessment of its estimate's precision. The unadjusted recalculation can add an effect-size perspective from the posted counts, but it cannot reproduce the sponsor's regression analysis. These limitations constrain interpretation of both the overall evidence and the consistency of findings across outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: High-Dose Versus Standard-Dose Oseltamivir to Treat Severe Influenza and Avian Influenza — NCT00298233.
• Registry record last updated 2014-06-06; status last verified 2014-05.
• Results first posted 2014-05-22.
• 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

NCT00298233 is listed as a completed, phase II, randomized, triple-masked, parallel-group trial sponsored by NIAID. The registry reports enrollment of 326 and compares high-dose with standard-dose oseltamivir in hospitalized patients with severe human influenza or avian influenza. Adult and child cohorts are described, with treatment planned for 5 to 10 days.

The primary endpoint is day-5 viral RNA negativity by RT-PCR among randomized patients with RT-PCR proven influenza. The posted counts yield a positive unadjusted risk difference, but its interval includes zero. The registry's own analysis reports p = 0.42. Numerical findings are posted for some, but not all, secondary outcomes. Missing-data procedures, multiplicity handling, and the original design assumptions are not reported in the registry record.