Trial of Intravenous Azithromycin to Eradicate Ureaplasma Respiratory Tract Infection in Preterm Infants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Intravenous Azithromycin to Eradicate Ureaplasma Respiratory Tract Infection in Preterm Infants (NCT01778634), a randomized phase 2 study. The primary outcome is Number of Participants With Survival And Transfer From NICU With Microbiological Eradication of Ureaplasma.

2. Clinical Question

The question joins a microbiological outcome with survival. Eradication alone is not the full primary endpoint: an infant must meet the registry definition of survival as well as the definition of bacterial clearance for the combined outcome. This makes the primary result a measure of achieving both conditions, rather than a direct estimate of the clearance result among all infants regardless of survival.

The record describes follow-up for the duration of the hospital stay, with an expected average of 10 weeks. It also lists outcomes concerning respiratory support, pulmonary health, survival and neurodevelopment. Those outcomes address other dimensions of the infants’ course, but they do not replace the primary question or change its combined definition.

3. Trial Design

This was a randomized, parallel-group, phase 2 trial comparing intravenous azithromycin with placebo. The official title describes it as phase IIb, randomized, placebo-controlled and double-blind; the registry also records quadruple masking. Enrollment was 121. The sponsor was University of Maryland, Baltimore, and the trial status is completed.

The azithromycin arm received intravenous azithromycin at 20 mg/kg every 24h x 3 days, with the concentration recorded as 2 mg/ml. The comparator was placebo, described as 5% dextrose. The registry gives no further detail about allocation concealment, the precise roles covered by quadruple masking, or procedures used to maintain masking, so those features cannot be characterized further from the record.

The study start is recorded as 2013-07 and primary completion as 2016-12. The primary outcome follow-up was for the hospital stay, expected to average 10 weeks. The primary outcome definition combines survival to discharge or transfer from the neonatal intensive care unit with microbiological eradication, defined through negative cultures. Secondary outcomes include events measured at 36 weeks postmenstrual age and later follow-up periods, as well as durations of respiratory support and oxygen supplementation.

Details of the original sample-size justification, target effect, and trial-specific assumptions are not reported in the registry record. The planning illustrations associated with the posted results are recalculations from the observed effect and should not be read as evidence of the assumptions that guided the original trial design.

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 Survival And Transfer From NICU With Microbiological Eradication of Ureaplasma, measured over Participants will be followed for the duration of hospital stay, an expected average of 10 weeks.

The primary endpoint is the number of participants with both survival and transfer from the NICU with microbiological eradication of Ureaplasma. The registry defines survival as being alive at discharge or transfer from the NICU. It defines bacterial clearance as 3 negative cultures obtained 2 and 5 days post-third dose and 21 d of age. Follow-up is listed as the duration of the hospital stay, with an expected average of 10 weeks.

This combined endpoint is used to capture two conditions relevant to the trial question in a single outcome. A result counted for the endpoint requires both survival to the stated point and evidence meeting the microbiological clearance definition. Consequently, it should not be interpreted as the eradication rate alone, nor as a survival outcome alone. The endpoint does not report the separate contribution of each component to the combined result.

In the posted results, 37 of 61 participants in the placebo group and 55 of 60 in the azithromycin group met the endpoint. The unadjusted risk difference is 0.310, with a 95% confidence interval from 0.169 to 0.451 and p < 0.001. The registry also reports a Cochran-Mantel-Haenszel odds ratio analysis. The outcome definition and analysis therefore need to be kept together when interpreting the effect: the result concerns the combined endpoint as recorded, under this trial’s follow-up and definitions.

7. Results Posted in the Registry

• Azithromycin: 91.7% (55/60) versus 60.7% (37/61) on control; risk difference 31.0 percentage points (95% CI 16.9 to 45.1), risk ratio 1.51 (1.22–1.88); 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.

Number of Participants Who Survived Until 36 Wks Postmenstrual Age With Physiologic Defined Bronchopulmonary Dysplasia (BPD) at 36 Weeks Post Menstrual Age

• 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:
  • Azithromycin: 44.6% (25/56) versus 33.3% (18/54) on control; risk difference 11.3 percentage points (95% CI -6.8 to 29.4), risk ratio 1.34 (0.83–2.16); unadjusted two-proportion z-test p = 0.224.
• 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.

Number of Participants With Death or Neurodevelopmental Impairment

• 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:
  • Azithromycin: 47.2% (25/53) versus 32.7% (17/52) on control; risk difference 14.5 percentage points (95% CI -4.0 to 33.0), risk ratio 1.44 (0.89–2.34); unadjusted two-proportion z-test p = 0.130.
• 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.

Number of Participants With Pulmonary Impairment

• 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:
  • Azithromycin: 25.0% (15/60) versus 19.7% (12/61) on control; risk difference 5.3 percentage points (95% CI -9.5 to 20.1), risk ratio 1.27 (0.65–2.48); unadjusted two-proportion z-test p = 0.482.
• 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 secondary outcomes broaden the clinical picture beyond the primary combined endpoint, but they do not measure the same event. They include outcomes related to bronchopulmonary dysplasia, death or neurodevelopmental impairment, pulmonary impairment, respiratory support, oxygen, and other events. Their timeframes vary, and some outcomes are available only for participants assessed at their specified follow-up.

Across the secondary results reported in detail, the unadjusted estimates tend toward more events in the azithromycin group, but their confidence intervals include no difference. The registry’s reported analyses likewise do not show a clear statistical distinction for the secondary outcomes described in detail. This is a broad reading of their pattern, not a substitute for considering each outcome’s definition, follow-up, estimate, and analysis separately.

These results do not contradict the primary finding because they address different outcomes and use different assessment times. Nor do they independently confirm it: secondary measures can be correlated with one another, and a pattern across outcomes is not equivalent to a prespecified combined analysis. The primary endpoint remains the main trial question recorded in the registry.

Unadjusted secondary results carry less weight when many outcomes are considered because repeated testing increases the opportunity for apparently notable findings by chance. The registry record does not report a multiplicity strategy or indicate how the secondary outcomes were prioritized. The secondary findings should therefore be treated as supportive or exploratory context, with attention to uncertainty and the analysis methods recorded for each outcome.

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

• Number of Participants Who Survived Until 36 Wks Postmenstrual Age With Physiologic Defined Bronchopulmonary Dysplasia (BPD) at 36 Weeks Post Menstrual Age
• Number of Participants With Death or Neurodevelopmental Impairment
• Number of Participants With Pulmonary Impairment
• Number of Participants Who Died
• Duration of Positive Pressure Support
• Duration of Oxygen Supplementation
• Number of Participants Who Experienced Air Leaks
• Number of Participants Who Received Postnatal Steroids

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

For a binary outcome, a risk is the proportion of participants in a group who experienced or met the outcome. The risk difference compares the two group risks by subtracting the comparator risk from the intervention risk. It is expressed on the probability scale, so values above no difference indicate a higher observed outcome frequency in the intervention group under that subtraction convention. A risk difference does not adjust for other variables unless the method explicitly does so.

The primary unadjusted recalculation is a risk difference of 0.310, with a 95% confidence interval from 0.169 to 0.451. The event counts are 37 of 61 in the placebo group and 55 of 60 in the azithromycin group. These are the observed data supporting that simple comparison. The estimate describes the difference in the proportions meeting the combined endpoint, not a difference in the number of participants and not an effect on eradication considered separately.

How does an odds ratio differ?

An odds ratio compares the odds of an outcome between groups rather than comparing the proportions directly. Odds are formed from the frequency of the event relative to the frequency of its absence. The odds ratio is therefore on a different scale from the risk difference. It can describe the direction and relative strength of an association, but it should not be read as an absolute percentage-point change or as a risk ratio.

The registry reports a Cochran-Mantel-Haenszel odds ratio for the primary endpoint. This is a method for combining group comparisons across strata. The strata used and other implementation details are not reported in the registry record. The reported odds ratio of 7.51 is accompanied by a 95% confidence interval from 2.53 to 22.27 and p < 0.001. The method and scale should be considered when comparing this result with the unadjusted risk-difference recalculation.

What does a confidence interval contribute?

A confidence interval conveys the precision of an estimate under the statistical method used. It gives a range of values compatible with the data and method at the stated confidence level; it is not a guarantee that the true effect lies in that range. A narrower interval generally indicates greater precision than a wider interval on the same scale. Whether an interval includes the null value is also relevant to interpreting a difference, but interval width and the possible magnitude of effects matter beyond that threshold.

For the primary risk difference, the reported interval is entirely above no difference. The secondary risk-difference intervals reported in detail extend across no difference. These patterns describe the estimates and their uncertainty; they do not resolve the clinical importance of the effects. The statistical method, outcome definition, and available participants all contribute to the interpretation.

Why distinguish reported analyses from recalculations?

The unadjusted recalculations use the posted group counts and are useful for describing simple between-group contrasts on a common scale. They are not a substitute for the sponsor’s own analysis. The sponsor reports a Cochran-Mantel-Haenszel analysis for the primary outcome, while the recalculation is an unadjusted risk difference. Different methods can produce different estimates because they answer the comparison on different scales and may handle stratification differently. The registry does not report enough detail to reconstruct every element of the sponsor’s analysis.

For secondary outcomes, the registry records generalized estimating equations for some analyses and generalized estimating equations with multiple imputation for pulmonary impairment. Generalized estimating equations are a framework for estimating population-average associations, often used when observations are correlated or when modeling repeated data. The record does not specify the correlation structure or all model details. Multiple imputation is a general approach for addressing missing values by replacing them with multiple plausible values under a stated modeling process; its validity depends on assumptions and implementation. The details needed to assess those assumptions are not reported in the registry record.

The posted recalculations are unadjusted. They do not include additional covariates or imputation unless explicitly stated as part of a sponsor-reported analysis. They are descriptive supplements to the reported analyses, not a reason to disregard the trial’s own inferential method.

11. Confidence Intervals and Precision

Precision is most directly assessed by considering the estimate together with its confidence interval. For the primary unadjusted risk difference, the estimate is 0.310 and the 95% confidence interval extends from 0.169 to 0.451. The whole interval lies above no difference. Its span nevertheless allows a range of possible effect sizes, so the point estimate should not be treated as exact.

The sponsor’s primary odds ratio is 7.51, with a 95% confidence interval from 2.53 to 22.27. This interval is also entirely on the side corresponding to higher odds in the azithromycin group. It is on the odds-ratio scale, however, and cannot be directly compared numerically with the risk-difference interval. The reported p-value is < 0.001.

For secondary outcomes, the posted unadjusted risk-difference intervals include values on both sides of no difference. This indicates that the data are compatible with differing directions and magnitudes for those outcomes under the unadjusted comparisons. It is not proof that the groups are equivalent. The intervals also should not be read as if they account for testing multiple outcomes.

Confidence intervals describe statistical uncertainty under a chosen method; they do not incorporate every source of uncertainty. The registry does not report all details of missingness, analysis populations, or the original analysis plan. Those omissions, along with the combined definition of the primary endpoint, constrain how fully the precision and interpretation can be evaluated.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original sample-size justification. The original design assumptions are not reported in the registry record. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. For the binary outcomes, the figures are participants per arm; the rule for time-to-event displays is total events, but the outcomes discussed in these planning illustrations are not time-to-event outcomes.

The 80% power column describes the number of participants per arm that the stated calculation estimates would be needed for an 80% chance of detecting the assumed effect, if that effect and the calculation assumptions were correct. The 90% power column gives the corresponding planning number for a higher chance of detecting that assumed effect. These are design calculations, not probabilities that the observed result is true or that the trial succeeded.

The rows scale the effect to 100%, 75%, and 50% of the observed effect. The displayed participant requirements rise as the assumed effect becomes smaller. This is the expected general relationship: smaller differences are harder to distinguish from sampling variation and therefore require more information, often through larger group sizes. The figures do not establish what effect the investigators considered important when planning the trial.

These calculations are planning illustrations, not observed power. Observed power calculated from an observed effect would largely re-express the result and its uncertainty rather than provide an independent measure of evidence. Confidence intervals and the prespecified analysis are more useful for interpreting the precision of the trial’s findings.

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 = 0.607; treatment proportion p₁ = 0.917; average p̄ = 0.762.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6026 = 1.1811.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5613 = 0.4724.
4. n = (1.1811 + 0.4724)² / (0.3101)² = 28.4, rounded up to 29 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 <- 0.60655737704918                          # control proportion
p1 <- 0.916666666666667                          # 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(1778634)
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 = 29 (80% power), 38 (90% power)
 75% of observed effect: n per arm = 57 (80% power), 76 (90% power)
 50% of observed effect: n per arm = 140 (80% power), 187 (90% power)
power.prop.test: 28.4 
Simulated power at n = 29 per arm: 0.825 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s reported primary analysis is a Cochran-Mantel-Haenszel comparison, with an odds ratio of 7.51, a 95% confidence interval from 2.53 to 22.27, and p < 0.001. The recalculation from the posted counts is an unadjusted risk difference of 0.310, with a 95% confidence interval from 0.169 to 0.451 and p < 0.001. Both results point in the same direction for the primary combined endpoint, but they use different effect scales and statistical methods.

The risk difference directly compares the observed group proportions. The Cochran-Mantel-Haenszel method combines comparisons across strata; the registry does not report the strata or enough detail to reproduce the analysis. Because the estimates are not on the same scale, their numerical sizes should not be treated as competing estimates of the same quantity.

The registry’s discrepancy flag is false. The unadjusted recalculation is therefore best read as a transparent descriptive contrast from the posted counts, while the sponsor’s reported analysis remains the trial’s stated inferential analysis. The record does not supply enough methodological detail to reconcile the calculations beyond their different scales and methods.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 18 outcome measures and 17 analyses. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a strategy for controlling the overall chance of false-positive findings across the analyses. Without that information, the reported p-values should be interpreted as results for their individual analyses rather than as evidence that the full family of outcomes was controlled at a stated error rate. The distinction matters particularly for secondary outcomes, where several questions are considered.

The primary endpoint is clearly identified in the record, which helps distinguish the main trial question from the secondary measures. However, the planned sequence of testing, if any, and the handling of multiple comparisons are not reported in the registry record. It is therefore not possible to determine from this record whether a formal hierarchy or adjustment was used outside the information presented.

The record does not specify whether the primary analysis followed an intention-to-treat, modified intention-to-treat, per-protocol, or another analysis population. Nor does it report detailed participant flow for the primary endpoint or explain how participants with unavailable cultures or outcome assessments were handled. These details are important because the primary outcome requires both microbiological assessment and survival to discharge or transfer.

Missing-data methods are not reported for the primary endpoint. The registry does record generalized estimating equations with multiple imputation for the pulmonary impairment outcome, but it does not describe the imputation model, assumptions, or missingness pattern. That report should not be taken to mean that the same approach was used for other outcomes.

These omissions limit assessment of robustness and the relationship between analyses. They do not alter the posted counts and reported estimates, but they leave uncertainty about analysis populations, missingness, and the broader interpretation of multiple outcome tests.

16. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: patent ductus arteriosus (28.3%), retinopathy of prematurity (19.0%), sepsis (14.8%), respiratory distress (9.8%), anemia (9.8%).

The registry reports serious adverse events affecting 39 of 61 participants in the placebo group and 44 of 60 in the azithromycin group. Other adverse events affected 51 of 61 participants in the placebo group and 51 of 60 in the azithromycin group. Deaths are recorded as 6 in the placebo group and 5 in the azithromycin group. These are reported event figures and should be read with their group denominators.

The listed serious adverse event terms include Patent Ductus Arteriosus at 28.3%, Retinopathy of prematurity at 19.0%, Sepsis at 14.8%, Respiratory Distress at 9.8%, Anemia at 9.8%, and Cholestasis at 8.3%. The registry does not provide an arm-specific breakdown for these terms in the record, so they should not be attributed to one group or used to compare groups. The terms may also represent events rather than mutually exclusive participants.

These figures describe what was recorded; they do not by themselves establish whether an event was caused by study treatment. Further detail about event timing, severity criteria, relatedness, and statistical comparison is not reported in the registry record.

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

The primary result indicates that, in this completed randomized trial, the observed proportion meeting the combined endpoint was higher in the azithromycin group than in the placebo group. The unadjusted estimate and its confidence interval are consistent with a positive difference on the risk-difference scale, and the sponsor’s reported odds-ratio analysis also favors the azithromycin group. The result concerns the registry-defined combination of survival to NICU discharge or transfer and microbiological eradication.

It does not isolate the microbiological component from the survival component. The record does not provide a separate primary estimate for each component, so the combined result cannot establish how much each contributed. It also does not establish that the same result would apply to different populations, settings, treatment schedules, or outcome definitions. The trial population is described as preterm infants born at 24 to 28 weeks gestation with Ureaplasma respiratory tract infection.

The secondary findings are more uncertain and cover distinct outcomes and timeframes. Their unadjusted intervals include no difference, and the registry does not report a multiplicity strategy. They should not be treated as definitive evidence either for or against differences in every secondary outcome. Likewise, adverse-event counts describe the recorded experience but do not establish causation.

Statistical significance is not a measure of clinical importance, and the confidence interval does not resolve that question. The registry record does not report a minimum clinically important difference or other threshold for judging the importance of the observed effect. It also does not provide the full protocol, analysis populations, or complete missing-data methods needed for a comprehensive assessment of all analytic choices.

The appropriate reading is therefore bounded: the posted primary data show a difference in the combined endpoint favoring azithromycin under the recorded definitions, while uncertainty remains about its components, broader applicability, and the details of the analytic plan. This statistical description is not medical advice and does not determine an individual infant’s care.

18. Why This Trial Matters Statistically

This trial illustrates how an endpoint’s definition shapes what a result can mean. The primary outcome is not simply bacterial clearance or survival: it requires both survival to discharge or transfer and microbiological eradication under a specified culture definition. That distinction is important whenever a trial combines events that may have different clinical meanings or occur through different processes.

It also illustrates why effect measures should not be treated as interchangeable. The posted counts support an unadjusted risk difference, while the registry’s primary reported analysis is an odds ratio from a Cochran-Mantel-Haenszel method. Both can describe the direction of a group comparison, but each expresses the result differently and relies on its own analytic structure. Interpreting them requires knowing which scale and method are being discussed.

The contrast between the primary and secondary findings is a useful reminder that a statistically clear primary result does not make every related outcome clear. Secondary measures have different definitions, timeframes, and available observations. Their interpretation also depends on how multiple analyses were planned and reported, details not given in the registry record.

Finally, the record shows why uncertainty and reporting completeness matter alongside a point estimate. Confidence intervals communicate a range of plausible values under the analysis, while missing information about populations, multiplicity, and missing data limits a full audit of the results. Careful biostatistical interpretation keeps the observed result, its method, its precision, and its reporting limitations in view at the same time.

19. Limitations

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

The primary outcome combines survival to NICU discharge or transfer with microbiological eradication. Because the registry does not report separate primary analyses for those components, the combined estimate cannot show which component most influenced the result. The culture-based clearance definition and its stated collection times also make the endpoint specific to this trial’s operational definition.

The population is narrowly described as preterm infants born at 24 to 28 weeks gestation with Ureaplasma respiratory tract infection. The registry record does not provide enough information about recruitment settings or additional eligibility criteria to assess how closely the enrolled population represents other groups. The duration of hospital follow-up is described as an expected average of 10 weeks, while secondary outcomes extend to later assessment periods; observations and denominators therefore differ across outcomes.

Important analysis details are not reported in the registry record. These include the original sample-size justification, analysis population, missing-data handling for the primary endpoint, multiplicity strategy, and full details of the sponsor’s stratified analysis. The posted unadjusted recalculations cannot replace those missing elements.

The serious adverse-event figures are presented as affected participants, but the record does not provide sufficient detail on event-level timing, relatedness, or arm-specific frequencies for the listed serious terms. The safety data therefore support descriptive reporting, not causal conclusions. The registry’s completed status and posted outcomes do not resolve these reporting limitations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial of Intravenous Azithromycin to Eradicate Ureaplasma Respiratory Tract Infection in Preterm Infants — NCT01778634.
• Registry record last updated 2020-11-30; status last verified 2020-11.
• Results first posted 2018-05-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01778634 is a completed randomized, parallel-group, phase 2 placebo-controlled trial sponsored by University of Maryland, Baltimore. It enrolled 121 preterm infants with Ureaplasma respiratory tract infection and compared intravenous azithromycin with placebo. The registry records quadruple masking and identifies the trial in its official title as double-blind.

The primary endpoint combines survival through NICU discharge or transfer with microbiological eradication, defined by negative cultures. The posted counts were 37 of 61 for placebo and 55 of 60 for azithromycin. The unadjusted risk difference was 0.310, with a 95% confidence interval from 0.169 to 0.451 and p < 0.001. The sponsor’s reported Cochran-Mantel-Haenszel analysis gave an odds ratio of 7.51, with a 95% confidence interval from 2.53 to 22.27 and p < 0.001.

Secondary outcomes cover respiratory, survival, developmental, and other events. Their detailed unadjusted results are more uncertain. The registry does not report several elements needed for a full assessment, including the multiplicity strategy, primary analysis population, and missing-data methods for the primary endpoint.