Comparison of Fluconazole vs Voriconazole to Treat Fungal Infections for Blood and Marrow Transplants (BMT CTN 0101): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Fluconazole vs Voriconazole to Treat Fungal Infections for Blood and Marrow Transplants (BMT CTN 0101) (NCT00075803), a randomized phase 3 study. The primary outcome is Fungal-free Survival (Percentage of Participants Alive and Free From Proven, Probable, or Presumptive Invasive Fungal Infection) at 180 Days Post-transplant.

2. Clinical Question

3. Trial Design

The registry describes a Phase III, randomized, double-blind, multicenter, prospective, comparative study of fluconazole versus voriconazole for preventing fungal infections in allogeneic transplant recipients. Its parallel-group structure assigned participants to one of the two treatment arms. The registry reports an enrollment of 600 and an allocation ratio of 1:1. The primary analysis included all randomized patients. The posted arm counts are 295 for fluconazole and 305 for voriconazole.

Randomization was stratified by center and donor type, with donor type described as sibling or unrelated. Stratification means that the allocation process took those categories into account when assigning participants. The registry does not report further details about the randomization sequence or how allocation concealment was implemented. Masking is recorded as double; further details about which individuals were masked are not reported in the registry record.

The treatment regimens were not described as identical in route or schedule. Fluconazole was administered as 400 mg by mouth or intravenous drip. The registry describes oral voriconazole at 200 mg twice daily and intravenous voriconazole at 200 mg every 12 hours for the duration of intravenous therapy. The registry does not report additional treatment-duration details in the record summarized for this analysis.

The trial is listed as completed. Its recorded start was 2003-11, and its primary completion was 2006-09. These dates describe the registry record and do not supply further detail about recruitment or follow-up. The primary endpoint was assessed at 180 days post-transplant. Secondary outcomes included invasive fungal infections over one year, survival outcomes, use of other antifungal drugs, graft-versus-host disease, and the galactomannan assay. The registry lists 13 outcome measures and 12 posted secondary outcomes; no secondary analyses are listed as reported analyses.

The original sample-size justification, planned statistical analysis in full, and details of any interim analyses are not reported in the registry record. The planning illustrations associated with the posted results are not a substitute for those original design details.

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 were included in the analysis

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 Fungal-free Survival (Percentage of Participants Alive and Free From Proven, Probable, or Presumptive Invasive Fungal Infection) at 180 Days Post-transplant, measured over 180 days.

The primary endpoint is the percentage of participants alive and free from proven, probable, or presumptive invasive fungal infection at 180 days after transplant. It combines two kinds of outcome: being alive and having no qualifying invasive fungal infection by the assessment time. The endpoint is therefore a defined status at a specified follow-up time, rather than a measure of infection alone or a time-to-event estimate.

Fungal-free survival is relevant to the stated prevention question because it reflects both survival and freedom from invasive fungal infection. The registry’s definition is important for interpretation: a participant must meet both parts of the endpoint to count as fungal-free survival. The record says all randomized patients were included in the primary analysis, but does not give further detail about how missing endpoint information or events after the assessment time were handled.

The posted percentages are 74.9% for fluconazole and 78.2% for voriconazole. Each arm’s result has a 95% confidence interval, which conveys uncertainty around the arm-specific percentage. The endpoint does not, by itself, identify why a participant did or did not meet the combined status. Nor does the percentage alone show the timing of infections or deaths within the follow-up period. Those distinctions matter when relating this result to the separate secondary outcomes.

7. Results Posted in the Registry

• Voriconazole: 78.4% (239/305) versus 74.9% (221/295) on control; risk difference 3.4 percentage points (95% CI -3.3 to 10.2), risk ratio 1.05 (0.96–1.14); unadjusted two-proportion z-test p = 0.318.

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.

Frequency of Invasive Fungal Infections (IFI)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Voriconazole: 12.8% (39/305) versus 13.6% (40/295) on control; risk difference -0.8 percentage points (95% CI -6.2 to 4.6), risk ratio 0.94 (0.63–1.42); unadjusted two-proportion z-test p = 0.780.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voriconazole and the control. The interval gives the range of effects that remain compatible with the data.

Frequency of Use of Amphotericin B or Caspofungin

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Voriconazole: 24.3% (74/305) versus 30.2% (89/295) on control; risk difference -5.9 percentage points (95% CI -13.0 to 1.2), risk ratio 0.80 (0.62–1.05); unadjusted two-proportion z-test p = 0.104.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voriconazole and the control. The interval gives the range of effects that remain compatible with the data.

Failure to Engraft

• 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:
  • Voriconazole: 3.0% (9/305) versus 3.7% (11/295) on control; risk difference -0.8 percentage points (95% CI -3.7 to 2.1), risk ratio 0.79 (0.33–1.88); unadjusted two-proportion z-test p = 0.596.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voriconazole and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related aspects of infection prevention and transplant follow-up. They include invasive fungal infection frequency over one year, use of amphotericin B or caspofungin, failure to engraft, survival and relapse-free survival, graft-versus-host disease, and the galactomannan assay. These outcomes address different events and follow-up questions, so their estimates do not duplicate the primary fungal-free survival measure.

Across the posted secondary results, the arm-specific estimates do not show a single uniform pattern in favor of one assignment. For invasive fungal infection frequency and use of other antifungal agents, the point estimates are lower in the voriconazole arm; failure to engraft is also numerically lower in that arm. The posted confidence intervals for these comparisons include no difference. This broad description should not be mistaken for a conclusion about benefit or harm: the outcomes differ, and the estimates retain uncertainty.

The primary endpoint combines survival and freedom from invasive fungal infection at 180 days, whereas the secondary infection outcome is frequency over one year. Use of additional antifungal drugs is a treatment-related measure rather than an infection endpoint itself. Failure to engraft is a separate transplant outcome. Consequently, agreement or disagreement among these measures is not necessarily contradictory; each captures a different part of the clinical course.

The registry lists no reported secondary analyses. The displayed comparisons are unadjusted, and the record does not report a multiplicity plan. General statistical explanation: when many outcomes are examined, the chance of finding at least one apparently unusual result by chance can increase. Without a prespecified hierarchy or adjustment details, individual secondary p values carry less weight than a designated primary analysis. The secondary results are best treated as descriptive context and as questions that may warrant further study, rather than as independent confirmatory evidence.

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

• Frequency of Invasive Fungal Infections (IFI)
• Percentage of Patients With Invasive Fungal Infection at 100, 180, and 365 Days
• Overall Survival
• Relapse Free Survival
• Frequency of Use of Amphotericin B or Caspofungin
• Duration of Use of Amphotericin B or Caspofungin
• Time to and Severity of Acute and Chronic Graft vs Host Disease (GVHD)
• Utility of Galactomannan Assay in Diagnosis of Aspergillus and Response to Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each person either meets the stated fungal-free survival definition at 180 days or does not. The registry reports the percentage of participants meeting that definition in each arm. The arm-specific percentages are 74.9% for fluconazole and 78.2% for voriconazole. The reported arm sizes are 295 and 305, respectively. The registry also gives a 95% confidence interval for each percentage.

What does a percentage estimate?

General statistical explanation: a percentage estimates the proportion of a population with a particular outcome, using the trial participants as the observed sample. A percentage is not a guarantee that the same proportion would occur in every comparable group. Sampling variability means that another randomized study could yield different estimates even if it addressed the same question. The confidence interval communicates some of this uncertainty. It does not describe the range of outcomes for individual participants.

What does the risk difference express?

The comparison is reported as a risk difference, with voriconazole compared against fluconazole. General statistical explanation: a risk difference expresses the difference between the two arms’ event proportions on an absolute scale. The registry also supplies a p value for the unadjusted comparison. The p value is 0.318 for the primary outcome. It is a measure of how compatible the observed data are with a specified no-difference model, under the assumptions of the test. It is not the probability that the no-difference model is true, and it does not measure the size or clinical importance of an effect.

The registry does not report the detailed test or model used for the sponsor’s primary analysis. It also does not report an adjusted analysis of the primary endpoint. Therefore, interpretation should stay with the posted estimates, intervals, and unadjusted p value rather than presuming a particular regression model or adjustment procedure. The randomization was stratified by center and donor type, but the record does not say whether those factors were incorporated in the primary comparison.

Why report confidence intervals?

General statistical explanation: a confidence interval gives a range of estimates compatible with the data and the method used to construct it. A 95% confidence interval is not a statement that there is a 95% probability that the particular fixed population value lies in that observed interval. Its interpretation relies on the statistical procedure and its assumptions. In these results, arm-specific intervals accompany the percentages, while the posted comparison also has an interval for the between-arm risk difference. The limits of the arm-specific intervals overlap; comparing those intervals visually is not a substitute for the interval and test for the between-arm contrast.

For the primary comparison, a recalculated unadjusted analysis can be formed from the posted summary counts and arm sizes. Such recalculations are descriptive checks, not a replacement for the sponsor’s own analysis. The record does not flag a discrepancy for this result. When a discrepancy is flagged for any result, the sponsor’s own analysis takes precedence over a simple recalculation.

What is known about the analysis population?

The record states that all randomized patients were included in the primary analysis. This is useful information because it identifies the stated analysis population. It does not, on its own, reveal how missing endpoint data were classified or whether every randomized participant had an observed endpoint. The approach to missing data, withdrawals, and deviations from assigned treatment is not reported in the registry record. Further details of the analysis population for secondary endpoints are also not reported.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variation is greater than a statistical model expects. It is particularly relevant to some count or clustered-data models, because underestimated variability can make intervals too narrow and tests too optimistic. The posted primary endpoint is a binary percentage, and the record does not report a model or an over-dispersion assessment. There is no basis in the registry record to claim that over-dispersion was tested or that a correction was needed. The concept is relevant as a general modeling issue, not as a reported feature of this trial’s primary analysis.

What does double-blind describe?

The trial is recorded as double-blind. General statistical explanation: masking can reduce the influence of knowledge of treatment assignment on behavior, assessment, and outcome reporting. The registry does not specify which participants or study personnel were masked, how masking was maintained, or whether it was assessed. The record therefore supports the stated double-blind design classification, but not additional claims about its implementation.

The trial was randomized and parallel-group, with a stated 1:1 allocation ratio and stratification by center and donor type. General statistical explanation: randomization is intended to reduce systematic differences between assigned groups, while stratification can incorporate selected categories into the allocation process. These design features do not guarantee identical groups on every characteristic, nor do they eliminate uncertainty in the estimated treatment contrast. Baseline characteristics and the method used to handle the stratification in the analysis are not reported in the material summarized by the registry record.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. The primary arm-specific fungal-free survival estimates are 74.9% for fluconazole and 78.2% for voriconazole. Their 95% confidence intervals are 69.6% to 79.5% and 73.1% to 82.4%, respectively. These intervals show that the arm-specific percentages are estimates rather than exact population values. Their breadth reflects uncertainty, and their overlap alone does not settle the between-arm comparison.

The posted unadjusted p value for the primary comparison is 0.318. It is consistent with substantial uncertainty about the size and direction of the difference. The registry also reports a confidence interval for the risk difference. That interval crosses zero, so the posted comparison is compatible with no difference as well as with differences in either direction. The interval should be read as a range of values supported by the analysis, not as a range containing every plausible value with certainty.

General statistical explanation: confidence intervals tend to become narrower when estimates are based on more information and wider when the data are less informative. Precision is distinct from statistical significance and from clinical importance. A narrow interval can still include effects that matter to a decision, and a wide interval can leave important possibilities unresolved. The registry does not specify a threshold for a clinically important difference, so the clinical meaning of the range cannot be judged against a stated margin.

The completed enrollment was 600, while the posted primary arm sizes are 295 and 305. These figures indicate the scale of the randomized groups, but do not by themselves determine precision; the amount and pattern of endpoint information also matter. The registry does not report missing-data handling or an original precision target. The interval is therefore the most direct posted measure of uncertainty for this endpoint.

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 express required participants per arm for the binary outcomes. They are based on the observed effect and show planning for 100%, 75%, and 50% of that effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm that would give an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detecting it, so its required participant count is larger. These are planning concepts, not guarantees about what a future study will find. Smaller effects require more participants because they are harder to distinguish from random variation.

For these binary outcomes, the figures are participants per arm, not total events. The registry’s general planning note distinguishes these from time-to-event illustrations, which use total events; the outcomes discussed in these planning displays are binary. The illustrations are not the original design justification for this trial, and they are not observed power. Observed power is not a useful substitute for interpreting the effect estimate and its confidence interval. The relevant reading is that the displayed requirements depend on the chosen effect fraction and stated planning assumptions.

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 = 0.749; treatment proportion p₁ = 0.784; average p̄ = 0.766.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5984 = 1.1728.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5979 = 0.5032.
4. n = (1.1728 + 0.5032)² / (0.0345)² = 2,366.4, rounded up to 2,367 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 <- 0.749152542372881                          # control proportion
p1 <- 0.783606557377049                          # 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(75803)
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 = 2,367 (80% power), 3,168 (90% power)
 75% of observed effect: n per arm = 4,262 (80% power), 5,705 (90% power)
 50% of observed effect: n per arm = 9,709 (80% power), 12,996 (90% power)
power.prop.test: 2366.4 
Simulated power at n = 2,367 per arm: 0.802 (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 identifies a primary endpoint and lists secondary outcomes, but does not report a statistical plan for controlling multiplicity across those outcomes. It does not describe a testing hierarchy, a family of hypotheses, or a correction for multiple comparisons. The number of listed outcome measures is 13, and 12 secondary outcomes are posted. Those counts indicate that multiple outcomes were considered, but do not establish how the investigators planned to interpret their collective results.

General statistical explanation: testing multiple outcomes can increase the chance of an apparently positive finding arising from random variation when each is considered separately. Adjustment methods or a prespecified order of testing can address that concern, but they can also change the interpretation and precision of individual results. Since such methods are not reported in the registry record, the secondary comparisons should be read as exploratory or descriptive rather than as a set of confirmatory tests.

The primary analysis population is stated as all randomized patients. The registry does not report the handling of missing primary endpoint data, withdrawals, loss to follow-up, or deviations from assigned treatment. It is therefore not possible to determine from the registry record whether any missing observations were excluded, imputed, or handled by another procedure. The completeness of the primary endpoint data is not reported.

Analysis populations for the secondary outcomes are not reported. Nor does the record provide the detailed statistical methods for those outcomes, the handling of competing events, or the approach to censoring for time-to-event outcomes. These omissions do not invalidate the posted estimates, but they limit assessment of how the analyses were conducted and whether the same population and assumptions applied across outcomes.

The record also does not report interim analyses or stopping rules. No particular interim monitoring approach should be inferred from the trial’s Phase III designation or completed status. These unanswered points are relevant to transparency and interpretation, not proof that a specific problem occurred.

15. 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: hypoxia (15.3%), dyspnea (14.6%), hepatic dysfunction (5.8%), hypotension (5.4%), mucositis/stomatitis (5.2%).

The registry reports serious adverse events affecting 78 of 295 participants in the fluconazole arm and 73 of 305 participants in the voriconazole arm. It reports other adverse events affecting 196 of 295 and 199 of 305 participants, respectively. These are counts of participants recorded as affected, not a complete description of event severity, duration, timing, or causal relationship to treatment.

The most frequent serious-event terms listed are hypoxia at 15.3%, dyspnea at 14.6%, hepatic dysfunction at 5.8%, hypotension at 5.4%, mucositis/stomatitis at 5.2%, and hemorrhage at 4.1%. The registry excerpt does not identify the arm-specific distribution for these terms. The percentages should therefore be read as the listed serious-event frequencies, not as a comparison between assigned treatments.

Deaths are not reported in the adverse-event figures. The registry record does not provide additional detail about event attribution or the safety analysis method. These figures describe reported events during the trial; they do not establish whether an event was caused by a study drug.

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

The primary result describes the percentage of randomized participants who were alive and free from proven, probable, or presumptive invasive fungal infection at 180 days after transplant. The observed percentages were 74.9% in the fluconazole arm and 78.2% in the voriconazole arm. The unadjusted p value was 0.318, and the confidence interval for the between-arm risk difference includes no difference. The data therefore leave uncertainty about the size and direction of any underlying difference.

This result does not establish that the treatments are equivalent. Equivalence requires a prespecified acceptable range for differences and an analysis designed to test that question; no such margin or framework is reported in the registry record. Nor does a non-significant comparison prove that the treatments have identical effects. It means the posted analysis did not provide clear statistical evidence of a difference under its unadjusted comparison.

The endpoint is a combined status at a fixed follow-up time, not infection alone. It cannot show from the percentage alone whether the result reflects survival, infection, or both. The secondary infection endpoint covers a different time period, and the other secondary measures concern additional treatment use and transplant outcomes. Their results should not be substituted for the primary result.

The registry record also does not report the original sample-size justification, missing-data methods, detailed analysis plan, or a multiplicity procedure. Those gaps limit assessment of the analysis beyond the posted estimates. The trial’s randomized, double-blind design and the stated primary analysis population are relevant design features, but they do not remove the uncertainty expressed by the confidence intervals.

In general, statistical evidence is one part of interpreting trial results. Clinical importance depends on the size of effects that matter to patients and clinicians, the outcome definition, the quality and completeness of follow-up, and other evidence. The registry does not provide a clinical importance threshold for the primary contrast. Accordingly, the posted figures support a careful description of this trial’s observed outcomes, not medical advice or a definitive judgment about treatment choice.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through its estimate and uncertainty rather than through a single p value. The primary percentages are close in the observed data, while the confidence intervals and the unadjusted p value show that the comparison does not sharply determine the underlying difference. A result that is not statistically clear is not the same as evidence of equivalence, and that distinction is important in clinical research.

The endpoint also demonstrates how outcome definitions shape interpretation. Fungal-free survival combines being alive with having no qualifying invasive fungal infection at 180 days. A combined endpoint can be informative for a prevention question, but it does not reveal the separate contribution of each component. Related secondary measures therefore add context without being interchangeable with the primary endpoint.

The registry reports randomization, double masking, a parallel design, and stratification by center and donor type. These features describe how the study was structured, while the absent details about the original analysis plan, missing data, multiplicity, and sample-size justification limit what can be learned about the intended inferential framework. Recognizing what is and is not reported is part of sound statistical interpretation.

Finally, the planning illustrations emphasize that sample-size requirements depend on the effect one aims to detect and the assumptions used. Their figures are not evidence of the trial’s observed power and are not the original trial’s design rationale. Separating planning calculations from observed results helps prevent overinterpretation of a completed trial’s estimates.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific questions unanswered. The original sample-size calculation and its assumptions are not reported, so the enrollment cannot be judged against a stated target effect or precision objective. The planning illustrations based on observed effects do not resolve this omission and should not be mistaken for the study’s design rationale.

The detailed statistical analysis plan is not reported. In particular, the record does not say whether the primary comparison incorporated the randomization strata, how missing endpoint information was handled, or whether analyses followed other prespecified procedures. All randomized patients are stated to have been included in the primary analysis, but this does not explain the completeness of outcome data or the treatment of missing values.

The registry does not report a multiplicity strategy despite the range of secondary outcomes. No reported secondary analyses are listed. The secondary results should therefore be interpreted cautiously, and the record does not support treating individual secondary comparisons as confirmatory tests.

Further limitations include the absence of reported detail about baseline characteristics, adherence, treatment discontinuation, masking implementation, and the arm-specific distribution of the listed serious adverse-event terms. These details are not reported in the registry record summarized for this analysis, so no inference about their balance or completeness is warranted.

The primary endpoint is a combined status at 180 days, while the frequency of invasive fungal infections is separately reported over one year. Those definitions and timeframes differ. The registry record does not provide enough methodological detail to assess all potential consequences of that distinction, including how deaths and missing observations were incorporated into secondary analyses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Fluconazole vs Voriconazole to Treat Fungal Infections for Blood and Marrow Transplants (BMT CTN 0101) — NCT00075803.
• Registry record last updated 2023-01-04; status last verified 2022-12.
• Results first posted 2015-09-04.
• 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 III, randomized, double-blind, multicenter, prospective, parallel comparison of fluconazole and voriconazole for prevention of invasive fungal infections in allogeneic blood and marrow transplant recipients. Enrollment is listed as 600. The recorded start was 2003-11, and primary completion was 2006-09. Randomization was stratified by center and donor type, with a 1:1 allocation ratio.

The primary outcome was fungal-free survival at 180 days post-transplant, defined as alive and free of proven, probable, or presumptive invasive fungal infection. All randomized patients were included in the primary analysis. The posted percentages were 74.9% for fluconazole and 78.2% for voriconazole, with an unadjusted p value of 0.318.

The registry lists secondary outcomes across infection frequency, survival, other antifungal use, engraftment, graft-versus-host disease, and diagnostic assay utility. No secondary analyses are listed as reported. The original sample-size justification, detailed missing-data methods, multiplicity plan, and full statistical analysis plan are not reported in the registry record.