Azithromycin in Bronchiolitis Obliterans Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Azithromycin in Bronchiolitis Obliterans Syndrome (NCT01009619), a randomized phase 4 study. The primary outcome is Prevalence of Bronchiolitis Obliterans Syndrome (BOS).

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-group, placebo-controlled trial registered as a Phase 4 study. The sponsor was KU Leuven. The registry record lists 83 participants as enrolled, with 40 in the azithromycin arm and 43 in the placebo arm for the primary outcome. The trial status is completed. The recorded start was 2005-09, and primary completion was 2009-12.

Participants were assigned to azithromycin or a matching placebo. The active regimen began with daily dosing for 5 days and continued with dosing three times weekly until the end of the study. The placebo description specifies the same schedule. Quadruple masking indicates that the trial record identifies masking at four levels, but does not state in the record which roles those levels represent.

The main outcome was the number of participants with bronchiolitis obliterans syndrome at 2 years post-transplant, assessed in the intention-to-treat population. The registry also lists acute rejection incidence, infection incidence, pulmonary function, broncho-alveolar neutrophilia, and plasma C-reactive protein levels as secondary outcomes. Five secondary outcomes have posted results. Details of the protocol beyond the recorded design and outcome descriptions, including the original sample-size justification and the trial’s full statistical analysis plan, 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

Analysis population for the primary outcome, as defined in the registry: intention to treat 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 Prevalence of Bronchiolitis Obliterans Syndrome (BOS), measured over 2 years post-transplant.

The primary endpoint is the prevalence of bronchiolitis obliterans syndrome at 2 years post-transplant, expressed as a number of participants. The registry definition requires a sustained decrease in forced expiratory volume in one second, or FEV1, of at least 20% from the participant’s maximum post-operative value, with no other cause identified. In practical terms, the endpoint counts participants who meet this specified lung-function criterion during the stated follow-up period.

A defined endpoint helps make the comparison between randomized groups interpretable: each group is assessed against the same clinical definition and timeframe. A participant count also makes the outcome directly understandable as the number meeting the definition in each arm. The endpoint is a prevalence measure at a specified follow-up point, rather than a measure of how quickly the condition first occurred. The registry description does not provide additional detail on how sustained decline was operationalized, how competing causes were assessed, or how participants without an observed endpoint assessment were handled; these details are not reported in the registry record.

7. Results Posted in the Registry

• Azithromycin: 12.5% (5/40) versus 44.2% (19/43) on control; risk difference -31.7 percentage points (95% CI -49.7 to -13.6), risk ratio 0.28 (0.12–0.69); unadjusted two-proportion z-test p = 0.001.

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.

Acute Rejection Incidence Rate

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Azithromycin: mean 0.86 versus 0.78 on control; difference 0.08 (95% CI -0.51 to 0.67), standardized effect d = 0.06; z-test p = 0.790.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Azithromycin and the control. The interval gives the range of effects that remain compatible with the data.

Infection Incidence Rate

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Azithromycin: mean 0.95 versus 0.73 on control; difference 0.22 (95% CI -0.39 to 0.83), standardized effect d = 0.16; z-test p = 0.477.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Azithromycin and the control. The interval gives the range of effects that remain compatible with the data.

Pulmonary Function

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Azithromycin: mean 81.11 versus 75.28 on control; difference 5.83 (95% CI -4.01 to 15.67), standardized effect d = 0.25; z-test p = 0.246.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Azithromycin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes span event rates, lung function, broncho-alveolar neutrophilia, and plasma C-reactive protein. Five secondary outcomes have posted results, while the registry record lists additional outcome measures overall. The outcomes do not all point in one consistent direction, and the secondary results do not provide a single, coherent confirmation of the primary prevalence contrast. They should be viewed as complementary descriptions of post-transplant events and measurements rather than as interchangeable measures of the primary endpoint.

The secondary findings also differ in their statistical presentation. The registry lists corrected chi-squared results for acute rejection and infection, but does not include the corresponding test statistics, effect estimates, or intervals. Unadjusted recalculations based on the posted summaries are available for several outcomes, but they do not reproduce or explain the registry’s reported tests. This leaves uncertainty about the intended analysis and prevents a fully harmonized comparison across endpoints.

In general, secondary outcomes carry less weight than a prespecified primary outcome when many outcomes are examined. Each additional comparison creates more opportunities for an apparently notable result to arise by chance, particularly if no multiplicity procedure is used. The registry record does not report whether secondary analyses were adjusted for multiple testing. Accordingly, secondary results can help describe the broader pattern, but isolated findings should not be treated as independent proof of the primary result or as definitive evidence for a separate effect.

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

• Acute Rejection Incidence Rate
• Infection Incidence Rate
• Pulmonary Function
• Broncho-alveolar (BAL) Neutrophilia
• Plasma C-reactive Protein (CRP) Levels

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary outcome is binary at the participant level: each participant either met the registry definition of bronchiolitis obliterans syndrome by the specified follow-up assessment or did not. The posted arm values are event counts, not means. A risk difference describes the contrast between the event proportions in the two randomized groups on the absolute scale. The negative estimate indicates fewer recorded events in the azithromycin arm than in the placebo arm. Risk ratios and odds ratios describe the same contrast using relative scales. They can be useful complementary summaries, but they do not represent additional outcomes or independent evidence.

The primary comparison is reported as an unadjusted recalculation from the posted group summaries. An unadjusted comparison does not account for covariates or other adjustments unless those are specified separately. The registry record identifies the primary analysis population as intention to treat, meaning the stated analysis concerns participants according to their randomized assignment. The registry does not give enough detail to determine exactly how all participants were included if outcome data were unavailable.

What does a p-value describe?

In general, a p-value measures how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of the observed contrast. The primary unadjusted p-value is 0.001. Because the registry record does not provide the complete analysis plan, the p-value should be interpreted as the posted unadjusted result rather than as evidence that every possible analysis or source of uncertainty has been addressed.

How should the interval be read?

In general, a confidence interval gives a range of values compatible with the data and the method used to construct the interval. A narrower interval indicates more precision on the scale being estimated; a wider interval indicates greater uncertainty. The interval for the primary risk difference is -0.497 to -0.137. Its values are all negative, so the estimated direction is consistently toward lower observed prevalence in the azithromycin group within this interval. The registry record does not specify the confidence level for this primary interval in the posted comparison details, so no confidence percentage should be assigned to it.

Why does the outcome type matter?

The primary endpoint is a binary count outcome, whereas several secondary endpoints are continuous means with standard deviations. These outcome types call for different summaries and analysis approaches. A count of participants with an event answers how many met the endpoint definition; a mean and standard deviation describe the average level and spread of a measured quantity or rate. An incidence rate expressed as events per person per year is not the same quantity as the proportion of participants with at least one event. Reading the outcome unit is therefore essential when comparing results across endpoints.

In general, event-rate data can have a distribution that differs from the assumptions of a simple normal model, especially when values are highly variable or concentrated near zero. Over-dispersion means that variation is greater than a model expects; if not addressed, standard errors and p-values can be poorly calibrated. The registry record does not describe a model for over-dispersion or provide enough detail to determine whether one was considered for the secondary incidence-rate outcomes.

What do the secondary analyses report?

For acute rejection and infection incidence rates, the registry lists a corrected chi-squared analysis with p < 0.05, but does not provide a test statistic, effect estimate, or confidence interval for those reported analyses. Separately, unadjusted recalculations from the posted means and standard deviations give mean differences and associated intervals. Those recalculations are simple comparisons of the posted summaries; they are not a reconstruction of an undocumented model or a replacement for an analysis described by the trial investigators. The registry record does not explain the relationship between the listed corrected chi-squared tests and the continuous summaries, so the discrepancy in analysis presentation cannot be resolved from the record alone.

In general, when a result is recalculated from summary statistics, it can serve as a transparent descriptive check, but it may not match an analysis that uses participant-level data, covariate adjustment, repeated measures, or a different distributional model. Those details are not reported in the registry record. The sponsor’s own analysis takes precedence if a discrepancy is identified; the posted record does not flag a discrepancy for the primary comparison.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -0.317, with an interval from -0.497 to -0.137. The interval stays on the negative side of zero, so the reported range does not include a null difference. Its width also shows that the data remain compatible with a range of effect magnitudes rather than a single exact value. The interval should be read as uncertainty around the estimated group contrast, not as a range containing a guaranteed value for the true effect.

The relative measures add another scale of description. The risk ratio is 0.283, with an interval from 0.117 to 0.686; the odds ratio is 0.180, with an interval from 0.059 to 0.550. Both intervals remain below 1, the no-association value for these relative measures. These are alternative presentations of the same primary event data, so they should not be counted as separate replications.

In general, precision depends on the amount of information in the data, including the number of participants and the number of observed events. Here, the primary arm sizes are 40 and 43, and the event counts are 5 and 19. The registry record does not provide a confidence level for the primary intervals or a detailed description of their construction. That limits how specifically the intervals can be characterized beyond their reported bounds and direction. The intervals also do not capture uncertainties arising from unreported decisions about missing outcomes, outcome adjudication, or analysis choices.

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 original trial design calculation. For this binary endpoint, the figures are participants per arm, not a total across both groups. The planning 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 to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions are correct. The 90% power column gives the corresponding per-arm planning figure for a higher chance of detection. These are planning quantities, not a description of the trial’s achieved ability to detect an effect. This is not observed power.

The curve and table should be read as showing how the planning requirement changes when the target effect changes. Planning for a smaller fraction of the observed effect requires more participants per arm, because a smaller group difference is harder to distinguish from sampling variation. The figures are not predictions of what a future trial will observe and are not evidence that the observed effect is reproducible. They are illustrative calculations under the stated assumptions; different design choices or analysis methods could produce different planning needs.

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 = 0.442; treatment proportion p₁ = 0.125; average p̄ = 0.283.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6373 = 1.2492.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5967 = 0.5022.
4. n = (1.2492 + 0.5022)² / (-0.3169)² = 30.5, rounded up to 31 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 <- 0.441860465116279                          # control proportion
p1 <- 0.125                          # 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(1009619)
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 = 31 (80% power), 41 (90% power)
 75% of observed effect: n per arm = 60 (80% power), 80 (90% power)
 50% of observed effect: n per arm = 144 (80% power), 192 (90% power)
power.prop.test: 30.5 
Simulated power at n = 31 per arm: 0.822 (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 outcome and multiple secondary outcome measures. Examining several outcomes can increase the chance of observing a nominally notable result even when there is no underlying group difference for those outcomes. In general, multiplicity procedures can control the overall error rate across a defined family of tests, but they may also affect the interpretation of individual p-values and intervals. Whether such a procedure was planned or applied is not reported in the registry record.

The primary comparison is posted with an unadjusted p-value. The record does not describe whether the primary test was part of a broader testing strategy or whether its interpretation was adjusted for other outcomes or analyses. The secondary results likewise do not include a stated multiplicity plan. Therefore, secondary p-values should be read as individual comparisons, not as evidence that the chance of any false-positive result across the full outcome set has been controlled.

The primary population is identified as intention to treat, which refers to analyzing participants according to randomized assignment. However, the registry record does not report how missing endpoint observations were handled, whether all randomized participants had outcome data at the specified assessment, or whether imputation or sensitivity analyses were used. It also does not describe analysis populations for every secondary endpoint. These omissions matter because missing outcome data can affect the event counts and the comparability of groups, depending on the reasons for missingness and the analysis approach.

Other details relevant to interpretation are also not reported in the registry record, including the full statistical analysis plan, any interim analyses, and the original sample-size justification. These are reporting gaps, not evidence that a particular procedure was or was not used. Without those details, the posted results can be described and compared, but the full prespecification and robustness of the analyses cannot be assessed.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry records zero participants with a serious adverse event in both the azithromycin and placebo groups. For other adverse events, it records 3 participants in the azithromycin group and 0 in the placebo group. These figures describe the counts of participants affected, not the total number of event episodes. The registry does not list serious adverse event terms, and deaths are not reported in the registry record.

These counts are descriptive and should be interpreted in light of the group sizes and the limited detail available. The record does not provide event descriptions, severity or timing details for the other adverse events, or information about how events were assessed and attributed. Zero recorded participants with a serious event in these groups does not establish that no such events could occur, nor does it provide a complete safety profile. The available registry figures support only a narrow statement about the events recorded in this trial record.

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

The primary result describes a difference between randomized groups in the proportion of participants recorded as meeting the bronchiolitis obliterans syndrome definition at 2 years post-transplant. The observed counts and the reported risk difference indicate a lower recorded prevalence in the azithromycin arm. The interval and p-value describe statistical uncertainty for that comparison, but they do not remove uncertainty about how well the endpoint was observed or how the result would apply in other settings.

In general, randomization is designed to make treatment groups comparable at assignment, supporting a causal interpretation when the trial is conducted and analyzed appropriately. A registry summary alone does not show all aspects of trial conduct, adherence, loss to follow-up, outcome assessment, or analysis. The record identifies an intention-to-treat population for the primary endpoint, but does not explain missing-data handling or provide the full analysis plan. Those limits mean the posted result should be read as evidence about the recorded comparison, not as a complete account of every methodological consideration.

The primary endpoint is specifically defined by sustained FEV1 decline without another cause, and the result concerns prevalence at the stated follow-up time. It does not directly describe time to onset, the course of lung function for every participant, or other clinical outcomes. The secondary outcomes measure related but distinct features of follow-up and are not a substitute for the primary endpoint.

The result does not establish a mechanism, guarantee a similar result in another population, or resolve the balance of all possible benefits and harms. It also does not make the secondary comparisons conclusive. The statistical interpretation is therefore bounded: the registry’s primary data show a group difference in the measured endpoint, while the record leaves important questions about analysis details, missing data, and broader applicability unanswered.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters in clinical biostatistics. The primary outcome is not simply a general label for worsening lung function: it is tied to a sustained decrease in FEV1 of at least 20% from the participant’s maximum post-operative value, with other causes excluded. That operational definition determines which participants count as having the endpoint and sets the meaning of the reported group comparison.

It also demonstrates the value of presenting an absolute contrast alongside relative measures. The risk difference describes the difference on the event-proportion scale, while the risk ratio and odds ratio express relative comparisons. All are derived from the same event counts, and their distinct scales can shape how a result is understood. Intervals matter alongside point estimates because they show the range of effect values compatible with the data under the analysis method.

The registry’s presentation of secondary analyses highlights a reporting challenge. A corrected chi-squared test is listed for two incidence-rate outcomes, yet its numerical test detail is absent, while recalculations from posted continuous summaries give a different analytical framing. Without a clear account of the model and prespecified plan, readers cannot fully reconcile these outputs. Complete reporting of analysis methods, missing-data procedures, and multiplicity plans is important for evaluating how robust a result is.

Finally, the trial’s modest arm sizes and the range of planning illustrations underscore the difference between observed results and future design requirements. Sample-size planning depends on a target effect and explicit assumptions; an observed effect is not a guaranteed future effect. Keeping that distinction clear helps prevent planning calculations from being mistaken for evidence about the certainty or reproducibility of a trial finding.

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 arise from the available registry record. The trial enrolled 83 participants, and the primary outcome counts come from groups of 40 and 43. The record does not provide participant-level data, so independent verification of the endpoint classification, missingness, or model assumptions is not possible from the posted summaries alone.

The registry describes the primary outcome definition and identifies an intention-to-treat analysis, but does not report how missing assessments were handled, whether outcome adjudication was blinded, or whether sensitivity analyses were conducted. It does not include the complete protocol or statistical analysis plan, the original sample-size justification, or any interim analysis details. The amount of information available for assessing prespecification and analytic robustness is therefore limited.

Secondary reporting is incomplete. Some registry-reported tests have no effect estimates or test statistics, and the record does not explain the relationship between those tests and the posted summary-statistic recalculations. The handling of multiple comparisons is also not reported. These issues limit how much weight can be placed on isolated secondary findings or how directly they can be compared.

The primary endpoint is a prevalence measure at 2 years post-transplant, and the record does not provide further detail on endpoint timing or assessment for participants with unavailable data. Safety reporting is also sparse: event terms and deaths are not reported in the registry record. These constraints mean the results are informative about the posted comparisons, but the registry summary cannot answer every question about trial conduct, detailed safety, or applicability to other groups.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Azithromycin in Bronchiolitis Obliterans Syndrome — NCT01009619.
• Registry record last updated 2011-10-03; status last verified 2011-08.
• Results first posted 2011-08-25.
• 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 record describes a completed, randomized, quadruple-masked, parallel-group, placebo-controlled Phase 4 trial sponsored by KU Leuven. It enrolled 83 participants and compared azithromycin with placebo after lung transplantation. The primary endpoint was bronchiolitis obliterans syndrome prevalence at 2 years post-transplant, analyzed in the intention-to-treat population.

The posted primary counts were 5 participants in the azithromycin group and 19 in the placebo group. The unadjusted risk difference was -0.317, with an interval from -0.497 to -0.137 and an unadjusted p-value of 0.001. Secondary results and limited adverse-event counts are also recorded. Important details about missing data, multiplicity, and the original analysis plan are not reported in the registry record.