Neonates and Azithromycin, an Innovation in the Treatment of Children in Burkina Faso: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Neonates and Azithromycin, an Innovation in the Treatment of Children in Burkina Faso (NCT03682653), a randomized phase 4 study. The primary outcome is 6 Month Mortality - All Cause.

2. Clinical Question

The clinical motivation described in the registry record is persistent neonatal mortality in some regions of sub-Saharan Africa. Earlier mass-distribution studies among children aged 1-59 months had reported mortality reductions in other settings, but the record emphasizes that those findings did not answer the question of administration during the neonatal period. It also describes concern about possible infantile hypertrophic pyloric stenosis associated with macrolide exposure, while noting that observational evidence can be affected by confounding by indication. The randomized azithromycin-versus-placebo comparison was intended to address efficacy and safety in the neonatal period. The results should therefore be read as evidence about this trial’s assigned intervention, population, outcomes, and follow-up, rather than as a direct estimate for other ages or settings.

3. Trial Design

The registry identifies this as a Phase 4, randomized, parallel-group trial with quadruple masking. Its status is completed. The registry lists enrollment of 21832 and identifies the sponsor as the University of California, San Francisco. The recorded study start is 2019-04-11, and primary completion is listed as 2022-05-01. These record entries describe the trial’s registration and conduct at a high level; they do not establish how every operational feature was implemented.

Infants were assigned to a single dose of azithromycin or a single dose of placebo during their 8th to 27th days of life. The primary outcome was all-cause mortality at 6 months. Listed secondary outcomes include all-cause mortality at 12 months, vital status, change in weight over time, change in length over time, infantile hypertrophic pyloric stenosis, adverse events, and neonatal mortality. The registry lists 8 outcome measures, while the posted secondary results include 7 outcomes. The specific reason for that difference is not reported in the registry record.

Random assignment is designed to make treatment groups comparable on average at the time of assignment, including for factors that may not be measured. It does not guarantee identical groups, and it does not remove uncertainty from a finite trial. Parallel-group allocation means each infant is assigned to one study group rather than crossing over between treatments. Quadruple masking indicates that masking was recorded at four levels in the registry, but the identities of those roles and the detailed masking procedures are not reported in the registry record.

The registry record does not report the trial’s original sample-size justification, allocation ratio, sequence-generation procedure, concealment process, prespecified analysis plan, or details of protocol deviations. Although it provides planning illustrations based on the observed effects, those illustrations are not the trial’s original design assumptions. Interpretation of the findings therefore rests on the posted outcome summaries and the design features actually recorded, without assuming unreported procedures.

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 6 Month Mortality - All Cause, measured over 6 months.

The primary endpoint is all-cause mortality at 6 months, described as the number of participants with the outcome. It addresses whether infants assigned to the two study groups differed in the risk of death from any cause by the stated follow-up age. An all-cause endpoint counts deaths without requiring attribution to a particular disease or mechanism. This can make the endpoint more direct and less dependent on subjective cause-of-death classification, though the registry record does not report how deaths were ascertained or classified.

The primary comparison reports event counts and the number of participants in each group, as well as a risk difference. The risk difference expresses the absolute contrast in event proportions, with the comparison oriented as azithromycin relative to placebo. A negative estimate means the posted proportion was lower in the azithromycin group; it does not by itself show that the intervention caused the difference. The estimate must be interpreted together with its confidence interval and the study design.

Mortality at 6 months is relevant to the trial’s stated objective of assessing whether a neonatal dose was associated with reduced all-cause mortality. It is also distinct from neonatal mortality and from the listed 12-month mortality outcome: each refers to a different follow-up period. The registry’s primary endpoint description does not report a more detailed definition of the at-risk population, the follow-up completeness rules, or how missing vital-status information was handled. Those details are important for understanding exactly which participants contributed to the estimate, and are not reported in the registry record.

7. Results Posted in the Registry

• Azithromycin: 0.4% (42/9606) versus 0.5% (50/9684) on control; risk difference -0.1 percentage points (95% CI -0.3 to 0.1), risk ratio 0.85 (0.56–1.28); unadjusted two-proportion z-test p = 0.425.

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.

12 Month Mortality - All Cause

• 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: 0.5% (52/9534) versus 0.7% (64/9563) on control; risk difference -0.1 percentage points (95% CI -0.3 to 0.1), risk ratio 0.81 (0.57–1.17); unadjusted two-proportion z-test p = 0.271.
• 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.

Vital Status

• 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: 0.5% (52/9534) versus 0.7% (64/9563) on control; risk difference -0.1 percentage points (95% CI -0.3 to 0.1), risk ratio 0.81 (0.57–1.17); unadjusted two-proportion z-test p = 0.271.
• 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.

Change in Weight Over Time

• 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 23.20 versus 23.30 on control; difference -0.10 (95% CI -0.25 to 0.05), standardized effect d = -0.02; z-test p = 0.196.
• 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 cover mortality at a later follow-up, vital status, growth, and safety-related outcomes. Across the posted comparisons with numerical estimates, the pattern does not establish a clear separation between groups. The mortality-related summaries point in the same broad direction as the primary point estimate, while the growth comparison is close to no mean difference. Their uncertainty remains important, and none should be treated as an independent confirmation of the primary result.

Secondary outcomes help describe whether findings are broadly consistent across related measures and whether effects might differ by outcome or follow-up period. They do not have the same evidential role as the primary endpoint, which was the designated main question. The 12-month mortality result concerns a different follow-up period from the primary endpoint. Vital status is also posted at 12 months and has the same numerical summary as the 12-month mortality result in the registry record; the record does not explain the relationship between those entries. The weight outcome measures a continuous growth measure rather than mortality, so it addresses a different aspect of the study.

Multiple secondary comparisons create a multiplicity concern: when many outcomes are tested, some apparently notable result can occur even if there is no underlying effect. The registry record does not report a multiplicity adjustment or a hierarchy for confirmatory secondary hypotheses. The secondary estimates are therefore most useful as context and as a basis for further questions, not as definitive stand-alone evidence. The registry reports no secondary analyses, which limits what can be concluded about adjusted models, subgroup patterns, or other hypothesis-testing procedures. Interpret the overall pattern cautiously, giving the primary endpoint the greatest weight and avoiding claims based on a single secondary result.

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

• 12 Month Mortality - All Cause
• Vital Status
• Change in Weight Over Time
• Change in Length Over Time
• Proportion of Infants Developing Infantile Hypertrophic Pyloric Stenosis
• Adverse Events
• Neonatal Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

The primary comparison uses a risk difference: the event proportion in the azithromycin group minus the event proportion in the placebo group. It is an absolute measure, expressed on the same scale as the event risks. A negative value means the observed proportion was lower in the azithromycin group; a positive value would mean it was higher. Unlike a relative measure, the risk difference directly describes the size of the absolute separation between group risks. Its meaning depends on the event definition and follow-up period, which for the primary result are all-cause mortality at 6 months.

The posted primary risks are 0.004 for azithromycin and 0.005 for placebo, and the risk-difference estimate is -0.001. These are reported statistics, not a guarantee that the population risks differ by exactly that amount. The estimate is subject to sampling variability, and interpretation depends on its uncertainty interval as well as the design and outcome data.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the observed data under the method used to calculate it. It is not a list of all possible effects, and it does not assign a probability to the true effect being inside this particular interval. In repeated use of a valid interval procedure, the stated confidence level describes the long-run performance of the method. The registry provides an interval for the primary risk difference from -0.003 to 0.001. Because the range crosses zero, it includes both directions of difference, including no difference. This uncertainty makes the point estimate insufficient as a stand-alone conclusion.

How should a p-value be read?

The unadjusted p-value for the primary comparison is 0.425. In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It is not the chance that the null hypothesis is true, the chance that the result occurred “by chance,” or an assessment of clinical importance. The record labels this value unadjusted. It does not report the test procedure in sufficient detail to infer additional modeling or adjustment choices.

Why distinguish absolute and relative measures?

The comparison also includes relative risk and odds-ratio summaries. These compare groups using ratios rather than an absolute difference. A relative measure can describe proportional separation, while the risk difference describes absolute separation. Their numerical scales and interpretations are different, so the values should not be treated as interchangeable. For the primary outcome, the posted relative risk is 0.847 with a confidence interval from 0.562 to 1.275; the odds ratio is 0.846 with a confidence interval from 0.561 to 1.277. Both intervals include the no-association value of one. These results likewise leave uncertainty about the direction and magnitude of the population contrast.

Why does randomization matter?

Random allocation is intended to balance prognostic factors between groups on average, so that a comparison can be interpreted as the effect of assignment rather than merely as an association between treatment received and outcome. This rationale depends on proper implementation, adequate outcome follow-up, and analysis consistent with the assigned groups. The registry records randomization but does not report the sequence-generation or concealment procedures, the analysis population, or the handling of deviations. Those features should not be presumed from the masking or allocation labels alone.

Why can sparse outcomes be difficult to estimate?

When an outcome is uncommon, a relatively small number of events can have substantial influence on the estimated group difference. The primary event counts are 42.0 and 50.0. This limited event information is reflected in uncertainty: an estimate may point in one direction while the confidence interval still covers meaningfully different possibilities. For rare outcomes, the absolute risk difference can be especially sensitive to the event count, and additional details about follow-up and ascertainment help assess how much confidence to place in the comparison.

What does over-dispersion mean in general?

In general, over-dispersion occurs when outcome variability exceeds what a particular statistical model assumes. If ignored, uncertainty estimates can be too narrow, making findings appear more precise than they are. The primary endpoint is reported as a binary participant count, and the registry record does not report an over-dispersion assessment or a model specification. Over-dispersion should therefore not be asserted as a feature of this analysis; it is a general concept relevant when selecting and checking models for data with extra variability.

What can be concluded from the posted analysis details?

The registry provides group counts, summary measures, confidence intervals, and unadjusted p-values for posted comparisons. It does not report the detailed statistical analysis plan, covariate adjustments, missing-data procedures, interim analyses, or multiplicity strategy. Consequently, these summaries support a basic reading of the observed contrasts and their reported uncertainty, but not a reconstruction of every analytic decision. The registry record is the source for the stated result; unreported methods should not be inferred from the numerical output alone.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data constrain the estimated group difference. The primary risk-difference estimate is -0.001, and its 95% confidence interval runs from -0.003 to 0.001. The interval extends from a negative value to a positive value, so it includes no difference and allows effects in either direction. The point estimate is therefore not precise enough to settle the direction of the underlying difference.

The interval also conveys more information than the unadjusted p-value alone. A p-value can summarize compatibility with a no-difference model, but it does not show the range of effect sizes that remain plausible. The confidence interval makes that range explicit on the absolute risk-difference scale. It should not be interpreted as proof that every value inside the range is equally likely, or as a statement that the true effect has a particular probability of lying within it.

The relative risk and odds-ratio intervals also cross their respective no-association value of one. That agrees with the risk-difference interval in leaving the direction unresolved, although each measure uses a different scale. A wide interval is not evidence that the groups are identical; it indicates that the data do not sharply distinguish among a range of possible effects. Conversely, an estimate near no difference does not establish equivalence. An equivalence conclusion would require an appropriate prespecified margin and analysis, which are not reported in the registry record.

The small number of primary events relative to the denominators is relevant to precision: uncertainty can remain substantial even when many participants are enrolled if the outcome is uncommon. The registry record does not provide a confidence interval for the raw event counts or additional precision analyses. The most defensible reading is therefore limited to the posted interval and the uncertainty it expresses, without treating the point estimate as a definitive treatment effect.

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 illustrative calculations based on the observed effect, not a reconstruction of the trial’s original design. For the binary mortality outcomes and the continuous weight outcome, the figures are participants per arm. They are not total participants across both arms and are not total event counts. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The original design’s sample-size assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under those assumptions for a design intended to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning target for a higher chance of detection under the same stated assumptions. Neither column is a probability that the observed result is correct, and the figures do not describe the chance that this completed trial detected its true effect. These are planning calculations, not observed power.

Each planning row uses a different target effect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For the primary result, the displayed participants-per-arm figures are 119,080 and 159,414 for planning for 100% of the observed effect; 216,067 and 289,251 for planning for 75% of the observed effect; and 495,978 and 663,973 for planning for 50% of the observed effect, for 80% and 90% power respectively. The pattern illustrates a general principle: smaller effects require more participants to detect under otherwise unchanged assumptions. A curve displaying the same planning relationship should be read as a visualization of these assumptions, not as evidence about treatment efficacy or the trial’s actual power.

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 = 0.005; treatment proportion p₁ = 0.004; average p̄ = 0.005.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.0974 = 0.1909.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.0974 = 0.0820.
4. n = (0.1909 + 0.0820)² / (-0.0008)² = 119,079.6, rounded up to 119,080 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 <- 0.00516315572077654                          # control proportion
p1 <- 0.00437226733291693                          # 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(3682653)
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 = 119,080 (80% power), 159,414 (90% power)
 75% of observed effect: n per arm = 216,067 (80% power), 289,251 (90% power)
 50% of observed effect: n per arm = 495,978 (80% power), 663,973 (90% power)
power.prop.test: 119079.6 
Simulated power at n = 119,080 per arm: 0.801 (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 record does not report a multiplicity strategy for the primary and secondary outcomes. This matters because repeated testing across several outcomes increases the opportunity for at least one result to appear unusual under a collection of no-effect hypotheses. A prespecified testing hierarchy, adjustment procedure, or explicit designation of exploratory outcomes can help control how such findings are interpreted. Without a reported strategy, unadjusted secondary p-values should not be treated as if each were the sole confirmatory test.

Missing-data methods and analysis populations are also not reported in the registry record. The group denominators differ across posted outcomes and are smaller than the enrollment figure, but the record does not explain the reasons. Those differences could reflect outcome-specific availability or other processes; their cause should not be guessed. The record does not state whether the primary analysis used all randomized participants, a modified intention-to-treat population, or another population definition. It also does not describe how unknown vital status, incomplete follow-up, withdrawals, or protocol deviations were handled.

These omissions affect interpretation because outcome availability can influence an estimate if missingness is related to group assignment or outcome risk. Randomization does not automatically resolve bias from missing outcomes after assignment. Sensitivity analyses can assess how conclusions change under alternative assumptions, but such analyses are not reported in the registry record.

The detailed statistical plan, interim analyses, covariate adjustment, and model specification are not reported in the registry record. Their absence from the posted information does not establish that a procedure was or was not used; it means the approach cannot be verified from this record. The reported comparison should therefore be read as the available summary rather than as a fully documented account of analysis decisions. Further documentation would be needed to evaluate multiplicity control, missing-data robustness, and the exact analysis population.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: mortality within 28 d of treatment (0.1%), hospitalization within 28 d of treatment (0.1%), infantile hypertrophic pyloric stenosis (0.0%).

The registry’s adverse-event summary lists serious events among 10898 participants at risk in the azithromycin group and 10934 in the placebo group. It reports 29 serious adverse events in the azithromycin group and 15 in the placebo group. The summary also lists other adverse events among the groups, with 575 and 599 affected participants, respectively. These are reported counts and denominators; they should not be converted into a causal conclusion by comparing the raw totals alone.

The most frequently listed serious terms include mortality within 28 d of treatment and hospitalization within 28 d of treatment, each shown as 0.1%, and infantile hypertrophic pyloric stenosis, shown as 0.0%. These displayed percentages are rounded registry entries. The record does not provide enough detail in the adverse-event summary to establish severity definitions, adjudication procedures, event timing beyond the listed terms, or whether events were judged related to the assigned intervention.

The deaths listed in the adverse-event fields are not interchangeable with the primary endpoint counts: the denominators and reporting context differ, and the registry does not explain the relationship between those records. Safety summaries can identify events requiring attention, but they do not alone determine whether an intervention caused an event or whether groups differ in overall safety. Interpretation needs event definitions, follow-up completeness, and analysis methods, which are not reported in the registry record.

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

The posted primary result is an estimate of the difference in all-cause mortality by 6 months between infants assigned to a single neonatal dose of azithromycin and those assigned to placebo. The observed risk difference is negative, but its confidence interval includes no difference and extends in both directions. The result therefore does not provide a statistically clear distinction between the groups, while also not proving that their underlying risks are identical.

This finding does not establish that azithromycin reduces mortality, increases mortality, or has no effect. A non-significant result is not a demonstration of equivalence or safety, and the point estimate should not be treated as a settled causal effect. The amount of uncertainty matters: the posted interval leaves a range of possible differences unresolved. The trial’s randomization supports a comparison of assigned groups, but the record does not report enough information about outcome ascertainment, missing data, or analysis populations to assess those aspects in detail.

The result also has a defined scope. It concerns administration during the neonatal period, in infants enrolled in Burkina Faso, and the primary endpoint at 6 months. It does not directly answer questions about different ages, doses, settings, outcomes, or treatment schedules. The listed 12-month mortality and other secondary measures add context, but they do not change the status of the primary result or supply a confirmatory answer when multiplicity and analysis details are not reported.

Safety interpretation requires similar restraint. Serious-event counts and selected terms are posted, but raw counts do not establish causation, and the registry record lacks details needed to assess event attribution and completeness. Taken together, the results describe what was observed in this randomized comparison and how uncertain the estimates remain. They should not be turned into a treatment recommendation or a generalized claim beyond the populations and outcomes recorded.

17. Why This Trial Matters Statistically

This trial addresses a statistically challenging question: whether a neonatal intervention is associated with a difference in mortality when the primary outcome is uncommon. A large enrollment can still yield limited information about a rare event if the number of observed events is modest. The primary comparison illustrates why event counts, absolute risks, and uncertainty intervals should be read together rather than relying on enrollment alone or on the direction of a point estimate.

The randomized, masked, parallel-group design is suited to comparing assigned intervention and placebo while limiting some forms of bias. At the same time, a design label does not replace documentation of implementation, follow-up, outcome ascertainment, and analysis. Those details are not reported in the registry record, so the findings invite attention both to the result and to the completeness of reporting needed to assess it.

The study also connects two distinct statistical questions: estimating an effect and planning a future study to detect an effect. The posted planning illustrations show that smaller target effects call for substantially larger per-arm sample sizes under the stated assumptions. They are not evidence that the observed effect is real, nor do they describe the original trial’s design basis. Keeping estimation separate from planning avoids mistaking an uncertain observed result for a reliable design target.

Finally, the trial highlights the role of outcome hierarchy and multiplicity. A primary mortality outcome anchors interpretation, while several secondary endpoints can broaden understanding but also create more opportunities for chance findings. Without a reported multiplicity plan and detailed analysis strategy, the secondary evidence is appropriately read as supporting context rather than a series of definitive conclusions. These statistical distinctions matter when communicating results from clinical trials with important outcomes and persistent uncertainty.

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 of interpretation arise from what the registry record does not report. It does not give detailed procedures for random-sequence generation, allocation concealment, implementation of quadruple masking, or ascertainment of deaths and other outcomes. These details are relevant to assessing the risk of bias, but their absence from the record should not be taken as proof that the procedures were inadequate.

Outcome denominators vary across the primary and secondary results, and the registry does not explain those differences. Missingness, loss to follow-up, withdrawals, and the treatment of unknown vital status are not described. The analysis population and any sensitivity analyses are also not reported. As a result, the robustness of the estimates to incomplete outcome data cannot be evaluated from the posted summaries.

The record does not report the original sample-size rationale, statistical analysis plan, adjustment strategy, interim monitoring, or multiplicity handling. It also lists 8 outcome measures while 7 secondary outcomes are posted, without explaining the discrepancy. The posted comparisons include unadjusted p-values, but the exact statistical tests and any covariate adjustments are not specified. These limits make it difficult to assess prespecification and the full inferential framework.

The safety information is a summary of counts and selected terms. Definitions, adjudication, attribution to treatment, and completeness of reporting are not described. The safety denominators differ from those for the primary outcome, and the relationship between adverse-event mortality entries and primary mortality counts is not stated. These limitations support a cautious interpretation of safety comparisons and preclude treating the raw totals as causal evidence.

Finally, the results are specific to the recorded neonatal intervention, study setting, and follow-up periods. The registry summary does not provide enough detail to assess generalizability across different populations or care contexts. These considerations qualify the strength and scope of conclusions without negating the information contained in the randomized comparison.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Neonates and Azithromycin, an Innovation in the Treatment of Children in Burkina Faso — NCT03682653.
• Registry record last updated 2023-06-27; status last verified 2023-06.
• Results first posted 2023-06-27.
• 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 4, randomized, quadruple-masked, parallel-group trial comparing a single dose of azithromycin with placebo in infants administered treatment between 8 and 27 days of life. The primary outcome was all-cause mortality at 6 months. The posted primary risk difference is -0.001, with a 95% confidence interval from -0.003 to 0.001 and an unadjusted p-value of 0.425.

The interval includes no difference and effects in either direction, so the primary result is uncertain rather than a clear demonstration of benefit, harm, or equivalence. Secondary outcomes and adverse-event summaries add context but do not resolve that uncertainty. Important details about missing data, analysis populations, multiplicity, and the original design assumptions are not reported in the registry record.