Posaconazole for the Prevention of Influenza-associated Aspergillosis in Critically Ill Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Posaconazole for the Prevention of Influenza-associated Aspergillosis in Critically Ill Patients (NCT03378479), a randomized phase 4 study. The primary outcome is Number of Participants With IAA-infection at ICU Discharge.

2. Clinical Question

3. Trial Design

The registry describes a phase IV, randomized, non-blinded, parallel-group, multicenter interventional study. The listed enrollment is 88, and the study status is completed. The registry lists the start date as 2017-12-27 and primary completion as 2020-03-31. The posted primary-outcome groups have denominators of 37 for standard care plus posaconazole and 36 for standard care. How these outcome denominators relate to the listed enrollment is not reported in the registry record.

The intervention group received standard care for influenza pneumonia plus intravenous posaconazole prophylaxis. The regimen description specifies 2*300mg/d IV on day 1, followed by 1*300mg/d IV from day 2 for 7 days. The comparator was standard care for influenza pneumonia, with treatment at the investigators’ discretion. Oseltamivir was also at the investigator’s discretion. The registry describes the trial as non-blinded, so masking of participants or study personnel was not part of the design as recorded.

The stated objective was proof of concept: to assess whether antifungal prophylaxis could reduce influenza-associated aspergillosis in ICU patients with severe influenza. The primary outcome was the number of participants with infection at ICU discharge, assessed from ICU admission to discharge, approximately 21 days. The registry also lists outcomes concerning time to diagnosis, length of ICU and hospital stay, and mortality. Details of the randomization sequence, allocation concealment, original design assumptions, and analysis populations 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.

Overall Study

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 IAA-infection at ICU Discharge, measured over from date of admission in ICU assessed up to ICU discharge, approximately 21 days.

The primary endpoint counts participants who met the registry’s definition of influenza-associated aspergillosis infection by ICU discharge. A case required mycological evidence of Aspergillus, at least one compatible sign or symptom, and radiological abnormalities. This combines evidence of the organism with clinical and imaging features rather than counting a laboratory finding alone. The endpoint was assessed from ICU admission to ICU discharge, approximately 21 days.

Counting participants with an event gives a binary outcome: each participant either met the specified case definition during the assessment period or did not. The resulting group counts and proportions can be compared between the randomized groups. An endpoint tied to ICU discharge is relevant to the stated prevention objective because it records whether the defined infection was present during the ICU course. It also depends on the registry’s diagnostic definition and the timing of assessment; it does not measure every possible fungal infection or later infection beyond the stated assessment period.

The registry does not report further details about diagnostic adjudication, assessor blinding, or how incomplete endpoint assessments were handled. Those details matter when interpreting how consistently the case definition may have been applied across the groups.

7. Results Posted in the Registry

• Standard of Care: 11.1% (4/36) versus 5.4% (2/37) on control; risk difference 5.7 percentage points (95% CI -6.9 to 18.3), risk ratio 2.06 (0.40–10.54); unadjusted two-proportion z-test p = 0.375.

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.

ICU Mortality - Number of Participant Deaths

• 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:
  • Standard of Care: 25.0% (9/36) versus 18.9% (7/37) on control; risk difference 6.1 percentage points (95% CI -12.9 to 25.0), risk ratio 1.32 (0.55–3.17); unadjusted two-proportion z-test p = 0.530.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard of Care and the control. The interval gives the range of effects that remain compatible with the data.

Hospital Mortality - Number of Participant Deaths

• 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:
  • Standard of Care: 27.8% (10/36) versus 21.6% (8/37) on control; risk difference 6.2 percentage points (95% CI -13.6 to 25.9), risk ratio 1.28 (0.57–2.88); unadjusted two-proportion z-test p = 0.542.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard of Care and the control. The interval gives the range of effects that remain compatible with the data.

90-day Mortality - Number of Participant Deaths

• 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:
  • Standard of Care: 30.6% (11/36) versus 24.3% (9/37) on control; risk difference 6.2 percentage points (95% CI -14.2 to 26.7), risk ratio 1.26 (0.59–2.66); unadjusted two-proportion z-test p = 0.551.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard of Care and the control. The interval gives the range of effects that remain compatible with the data.

The posted mortality comparisons show a consistent direction in their point estimates: the observed mortality proportions are numerically higher in standard care than in the posaconazole-plus-standard-care group. The confidence intervals for these comparisons include no difference and extend across both directions. This shared pattern is descriptive; it does not establish a mortality benefit or a reliable group difference.

Mortality outcomes provide context alongside the primary infection outcome, but they measure different events at different points in care. ICU mortality, hospital mortality, and mortality at the stated follow-up cannot be treated as substitutes for the primary endpoint of influenza-associated aspergillosis at ICU discharge. Nor does the direction of the mortality estimates validate the primary result. Each outcome has its own event definition, assessment time, and uncertainty.

The registry lists secondary outcomes concerning time to IAPA diagnosis and length of ICU and hospital stay, as well as mortality. Quantitative results for the time and length-of-stay outcomes are not reported in the registry record. Thus, the overall secondary evidence is incomplete in the posted results; a pattern across the available mortality estimates cannot summarize outcomes for which numerical results are not reported.

Secondary findings generally carry less weight than a prespecified primary comparison, particularly when several outcomes are examined. Repeated testing without a reported strategy for handling multiplicity can increase the chance that at least one apparent finding arises by chance. The registry record does not report a multiplicity adjustment, and it does not report analyses for the listed secondary outcomes. The secondary estimates are therefore best used as supporting context and interpreted cautiously, rather than as independent confirmation of the primary comparison.

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

• Time to IAPA Diagnosis
• Length of ICU Stay
• Length of Hospital Stay
• ICU Mortality - Number of Participant Deaths
• Hospital Mortality - Number of Participant Deaths
• 90-day Mortality - Number of Participant Deaths

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary because the registry counts participants who met the infection definition by ICU discharge. For this kind of outcome, a group’s event count is interpreted in relation to the number of participants with outcome data in that group. The comparison presented is a risk difference: the event proportion in standard care minus the event proportion in posaconazole plus standard care. A positive estimate therefore means the observed proportion was higher in the standard-care group. The estimate is 0.057, and its confidence interval runs from -0.069 to 0.183.

What does a risk difference express?

A risk difference describes an absolute contrast between two observed event proportions. It is measured on the probability scale, so zero corresponds to no difference in the proportions. Values on either side of zero correspond to different directions of contrast. This measure is distinct from a relative measure, which expresses one group’s event probability in relation to the other group’s probability. Absolute and relative measures can both be useful, but they answer different questions and can appear more or less striking depending on how common the event is.

The registry comparison also lists a risk ratio and an odds ratio. These are relative measures: the risk ratio compares event probabilities, while the odds ratio compares event odds. Relative measures can be less intuitive when the outcome is uncommon, and they should be read with their confidence intervals rather than as standalone point estimates. The primary interpretation focuses on the risk difference because it directly expresses the absolute contrast between groups.

How should the p-value be read?

The posted p-value is unadjusted. In general, a p-value describes 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. A p-value does not replace the estimate and confidence interval: those show the direction, magnitude, and precision of the group contrast.

The unadjusted primary p-value is 0.375. This does not provide strong evidence against no difference under the unadjusted comparison, but it does not establish that the groups have identical outcomes. A non-significant result can reflect a small true difference, limited information, or both. The interval is therefore important: it includes zero and also allows differences in either direction.

Why does the confidence interval matter?

A confidence interval gives a range of effect estimates compatible with the data under the method’s assumptions. It is not a guarantee that the true effect lies within the displayed endpoints, and it does not identify which effect is correct. Wider intervals indicate less precision. For binary outcomes with few events, the estimate can be sensitive to the event counts, and the interval may remain wide even when the point estimate appears to favor one group.

The comparison is an unadjusted contrast based on posted group summaries. The registry record does not report whether additional covariate adjustment, stratification, or another model was part of a sponsor analysis. The random allocation is part of the design, but it does not remove the need to understand the analysis and its assumptions. The record also does not report how missing outcomes were handled or which analysis population was used.

What do secondary comparisons add?

The mortality outcomes are also binary counts, and their posted comparisons use risk differences. They offer context about outcomes during the ICU stay, at hospital discharge, and at the stated follow-up. They do not replace the primary endpoint: mortality and diagnosed aspergillosis are different outcomes, and results on one cannot be used as a direct estimate of the other. The registry lists additional secondary outcomes, but quantitative results for all listed outcomes are not present in the posted results described by this record.

Secondary comparisons should be treated cautiously when many outcomes are considered. Unless a testing strategy accounts for multiple comparisons, repeated testing can make chance findings more likely. The registry record does not report a multiplicity adjustment or a complete inferential analysis plan. General statistical interpretation therefore gives priority to the stated primary endpoint while treating the secondary estimates as contextual, not definitive evidence.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.057, with a confidence interval from -0.069 to 0.183. The interval includes zero, which represents no absolute difference, and also includes estimates on either side of zero. The data therefore do not locate the primary contrast precisely enough to determine its direction with confidence. The point estimate favors a higher observed proportion under standard care, but the interval leaves substantial uncertainty around that pattern.

Confidence intervals describe precision as well as direction. A narrow interval would indicate that the data constrain plausible values more closely; a broad interval leaves a wider range compatible with the observed data and method. Here the event counts are limited, so the estimate is not precise. The endpoints of the interval should not be treated as predictions or as a range guaranteed to contain the true effect.

The same caution applies to the secondary mortality comparisons. Their risk-difference intervals include zero and extend to both sides of it. This pattern indicates uncertainty rather than evidence that the groups are equivalent. The registry record does not report adjusted confidence intervals or a sponsor’s full statistical analysis for these outcomes. The displayed intervals should be interpreted as the posted, unadjusted comparisons, not as a complete accounting of every uncertainty in study conduct or outcome measurement.

Precision also concerns the scope of inference. The trial enrolled patients with severe influenza admitted to the ICU, and the registry record does not provide detailed characteristics that would establish how closely this group resembles other clinical settings. Even a more precise estimate would apply most directly to the study population and outcome definition; the current estimates are additionally limited by their breadth.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these binary outcomes, the displayed figures are participants per arm, not total participants. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. Time-to-event calculations, if present, are expressed as total events, but the outcomes are not time-to-event outcomes.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column applies the same idea at a higher chance of detection. These are design-planning quantities: they do not describe the probability that this completed trial found a true effect, and they are not observed power.

As the effect to detect becomes smaller, the calculation requires more participants per arm. That is because smaller differences are harder to distinguish from random variation. The planning figures depend on the assumptions and on the observed effect used as their starting point. They should not be taken as a recommendation or as proof that a future study with those numbers would reproduce the same result. The registry record does not report the sample-size assumptions used in the trial’s original design.

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 = 0.054; treatment proportion p₁ = 0.111; average p̄ = 0.083.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3893 = 0.7629.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3872 = 0.3258.
4. n = (0.7629 + 0.3258)² / (0.0571)² = 364.1, rounded up to 365 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 <- 0.0540540540540541                          # control proportion
p1 <- 0.111111111111111                          # 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(3378479)
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 = 365 (80% power), 487 (90% power)
 75% of observed effect: n per arm = 597 (80% power), 799 (90% power)
 50% of observed effect: n per arm = 1,227 (80% power), 1,642 (90% power)
power.prop.test: 364.1 
Simulated power at n = 365 per arm: 0.808 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, but the record does not report a complete statistical analysis plan or a procedure for controlling multiplicity. When researchers examine several outcomes, the chance of observing an apparently notable result by chance can increase. A prespecified hierarchy or adjustment can address that issue, but whether any such approach was planned or used is not reported in the registry record. The posted comparisons are described as unadjusted.

The registry record does not report how missing outcome data were handled, whether any participants lacked endpoint assessments, or how participants were assigned to analysis populations. It does not state whether the primary analysis followed intention-to-treat, per-protocol, or another population definition. The posted outcome denominators are available, but their relationship to the listed enrollment is not explained in the registry record. It would be inappropriate to infer the reason for that difference or assume a particular missing-data process.

Further analysis details are also not reported, including the randomization sequence method, allocation concealment, any covariate adjustment, and whether outcome assessors were blinded. The study itself is recorded as non-blinded, but the record does not clarify whether diagnostic assessment had separate safeguards against knowledge of assignment. Such details can affect the interpretation of a clinical endpoint that includes clinical signs and imaging as well as mycological evidence.

The record reports no posted analyses for the listed secondary outcomes in its analysis listing. Consequently, the available numerical comparisons should not be mistaken for a complete, prespecified analysis of all outcomes. These reporting gaps limit assessment of how outcomes were selected, how uncertainty was handled across multiple tests, and whether analysis decisions were made before results were known.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death (30.6%).

The serious adverse event figures report affected participants in each group: 9 in the posaconazole-plus-standard-care group and 11 in the standard-care group. The registry records 9 deaths in the intervention group and 11 in the standard-care group. Death is also listed as the top serious adverse event term, with 30.6% shown in the record. No other serious or other adverse event counts are listed for these groups in the posted figures.

These counts are descriptive and do not establish whether an event was caused by a study treatment. The record does not provide a causal attribution analysis, event-level descriptions, or a comparison adjusted for differences in follow-up or clinical status. Deaths during critical illness may arise for many reasons, and the counts alone cannot identify the role of posaconazole or standard care. The registry’s safety figures should therefore be read as reported event counts, not as proof of comparative safety or harm.

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

The posted primary data show fewer participants meeting the defined infection endpoint in the posaconazole-plus-standard-care group than in the standard-care group. The estimated risk difference is 0.057 in the direction of a higher observed proportion with standard care, but its confidence interval, from -0.069 to 0.183, includes no difference and effects in either direction. The unadjusted p-value is 0.375. Together, these results describe an uncertain comparison rather than a clear separation between groups.

The result does not establish that posaconazole prevents influenza-associated aspergillosis, and it does not establish that prophylaxis has no effect. The number of observed infections was limited, and the estimate remains imprecise. A non-significant result is not proof of equivalence. Likewise, the direction of the point estimate is not enough to claim a treatment benefit.

The study was non-blinded and used an endpoint requiring clinical, imaging, and mycological evidence. The registry record does not report additional details about diagnostic adjudication, analysis populations, missing data, or multiplicity. These omissions make it difficult to evaluate all potential sources of uncertainty beyond the interval around the unadjusted comparison.

The findings apply most directly to the population and care setting described in the registry: critically ill patients with severe influenza admitted to an ICU, receiving posaconazole plus standard care or standard care alone. The registry does not provide detailed participant characteristics to assess transportability to other settings. The mortality findings are separate secondary outcomes and do not answer the primary infection question. The overall interpretation should remain confined to the posted data and their substantial uncertainty.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an observed direction and a precise estimate. The primary point estimate places the event proportion higher under standard care, but the confidence interval includes no difference and extends to values on either side. A reader who focuses only on the counts or point estimate could overstate what the data establish; attention to the interval makes the uncertainty visible.

The trial also illustrates why a proof-of-concept study and a definitive comparative study serve different purposes. The stated objective was to examine whether prophylaxis could reduce influenza-associated aspergillosis in critically ill patients. The posted result contributes an estimate, but the limited event information does not provide a precise answer. Planning illustrations based on the observed effect show how strongly sample-size needs depend on the effect a future study aims to detect, while remaining separate from the original design assumptions, which are not reported.

Finally, the record highlights the importance of transparent reporting. Knowing how randomization was implemented, how the outcome was adjudicated, how missing data were handled, and how multiple outcomes were analyzed would help readers assess the comparison. The registry reports a non-blinded randomized design and a defined primary endpoint, but several analysis details are not reported. Statistically, the most responsible conclusion is not a treatment claim, but a description of the estimate, its uncertainty, and the limits of the available record.

18. Limitations

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

Several limitations are specific to the design and reporting of this trial. The registry records a non-blinded study, and the primary endpoint includes clinical signs or symptoms and radiological abnormalities alongside mycological evidence. The record does not report whether diagnostic assessment was blinded or how cases were adjudicated. Knowledge of assignment could matter for outcomes requiring clinical assessment, although the registry does not provide enough detail to determine whether it affected this endpoint.

The observed primary event counts are limited, and the confidence interval is broad. This leaves substantial uncertainty about the size and direction of the group difference. The study’s stated proof-of-concept objective does not remove that imprecision. The planning illustrations are based on the observed effect and are not a report of the sample-size assumptions used when the trial was designed.

Standard care was at investigators’ discretion, and oseltamivir could also be started at investigator discretion. The registry record does not provide further detail about how those decisions varied across participants or groups. This limits assessment of the treatment context and the comparability of care beyond random assignment.

Important reporting details are absent: analysis populations, missing-data handling, the randomization and concealment procedures, multiplicity methods, and quantitative results for several listed secondary outcomes are not reported in the registry record. The record lists enrollment of 88, while the primary outcome denominators are 37 and 36; it does not explain the relationship between these figures. No explanation should be inferred from the registry information alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Posaconazole for the Prevention of Influenza-associated Aspergillosis in Critically Ill Patients — NCT03378479.
• Registry record last updated 2025-04-08; status last verified 2025-03.
• Results first posted 2025-04-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed phase IV, randomized, non-blinded, parallel-group, multicenter study of posaconazole prophylaxis for influenza-associated aspergillosis in critically ill patients with severe influenza. Listed enrollment is 88. The primary endpoint was the number of participants with infection at ICU discharge, defined using mycological, clinical, and radiological evidence.

The posted primary comparison records 2 events among 37 participants receiving posaconazole plus standard care and 4 among 36 receiving standard care. The risk difference comparing standard care with the intervention group is 0.057, with a confidence interval from -0.069 to 0.183 and an unadjusted p-value of 0.375. The interval includes no difference, so the estimate remains uncertain.

The record also lists mortality and other secondary outcomes. Available mortality comparisons are descriptive, while quantitative results for some listed outcomes and important analysis details are not reported in the registry record.