Can Earlier BCG Vaccination Reduce Early Infant Mortality? A Randomised Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Can Earlier BCG Vaccination Reduce Early Infant Mortality? A Randomised Trial (NCT02504203), a randomized phase 4 study. The primary outcome is Non-accidental Mortality.

2. Clinical Question

3. Trial Design

The trial is listed as phase 4, randomized, open-label, and parallel-group. The registry record gives enrollment as 2332 and identifies Bandim Health Project as the sponsor. The record lists a start date of 2015-11, primary completion in 2021-06, and status as terminated. It does not report why the trial was terminated.

The intervention arm was assigned BCG and OPV at home visits, while the control arm received no vaccines at those visits. Both groups were described as receiving nursing care at the home visit, including cord and skin care, support for skin-to-skin contact, examination, and weighing. The record's intervention description names BCG-Denmark 1331 and BCG Japan as possible BCG formulations, but it is incomplete after the words “Dependent on”; the full intervention details are therefore not reported in the registry record.

The primary outcome was non-accidental mortality, measured as participants with the event, over the period between the home visit and the next BHP follow-up, subject to the specified stopping rules and 60 days of life. The posted counts were 7 in the intervention arm and 28 in the control arm. The corresponding arm sizes for this outcome were 1006 and 1206. The registry record does not report the original sample-size justification or the trial's planned statistical analysis in enough detail to assess those plans.

Randomization and parallel assignment describe how the study was structured, but the record does not report the sequence-generation method, allocation concealment, or masking of outcome assessment. Masking is listed as none. These details matter when assessing how assignment was implemented and how outcome information may have been collected.

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: Children entered the analysis on the date of enrolment or 24 hours of age, whichever came last, and remained in the analysis until whatever came first: the first subsequent visit by the BHP team, date of registering first non-trial vaccine after enrolment, death, migration, or 60 days of life.

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 Non-accidental Mortality, measured over 60 days after birth.

The primary endpoint is non-accidental mortality among participants during a defined early-life follow-up period. The registry record describes the interval as beginning at the home visit and ending at the next BHP follow-up, when unvaccinated children at home would be offered BCG, or at registration of a non-trial vaccine or 60 days, whichever came first. The population description adds that analysis began at enrolment or 24 hours of age, whichever came later, and stopped at the first subsequent BHP visit, registration of a first non-trial vaccine, death, migration, or 60 days of life.

This endpoint is a count of participants with the event, rather than a measure of time until an event or a repeated-event count. Mortality is a direct outcome and is clinically consequential, while limiting the timeframe makes the endpoint specific to early infancy. The non-accidental qualification distinguishes the endpoint from all-cause mortality, but the registry record does not report the classification procedure or how causes were adjudicated.

The posted comparison records 7 events among 1006 intervention-arm participants and 28 among 1206 control-arm participants. The risk difference is -0.016, with an interval estimate from -0.026 to -0.006. The record does not report the confidence level for this interval. Interpretation should retain the endpoint's precise definition and stopping rules: the result is not a comparison of mortality over all infancy or over a uniform follow-up period extending beyond the specified limits.

7. Results Posted in the Registry

• Intervention: BCG and OPV at Home Visits: 0.7% (7/1006) versus 2.3% (28/1206) on control; risk difference -1.6 percentage points (95% CI -2.6 to -0.6), risk ratio 0.30 (0.13–0.68); unadjusted two-proportion z-test p = 0.002.

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.

Non-accidental Hospital Admission

• 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:
  • Intervention: BCG and OPV at Home Visits: 0.7% (7/1006) versus 1.2% (15/1206) on control; risk difference -0.5 percentage points (95% CI -1.4 to 0.3), risk ratio 0.56 (0.23–1.37); unadjusted two-proportion z-test p = 0.196.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention: BCG and OPV at Home Visits and the control. The interval gives the range of effects that remain compatible with the data.

Severe Morbidity

• 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:
  • Intervention: BCG and OPV at Home Visits: 1.4% (14/1006) versus 3.0% (36/1206) on control; risk difference -1.6 percentage points (95% CI -2.8 to -0.4), risk ratio 0.47 (0.25–0.86); unadjusted two-proportion z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Intervention: BCG and OPV at Home Visits than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

All-cause Consultations

• 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:
  • Intervention: BCG and OPV at Home Visits: 10.0% (101/1006) versus 6.3% (76/1206) on control; risk difference 3.7 percentage points (95% CI 1.4 to 6.0), risk ratio 1.59 (1.20–2.12); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Intervention: BCG and OPV at Home Visits than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record lists secondary outcomes spanning hospital admission, severe morbidity, consultations, growth measures, vaccination scarring, cost-effectiveness, and cause-specific mortality. Numeric comparisons are posted for non-accidental hospital admission, severe morbidity, and all-cause consultations. The other listed outcomes do not have numeric results described in the posted comparison summaries, so their results are not reported in the registry record.

Across the three posted comparisons, the directions are mixed rather than uniformly aligned with the primary result. The hospital-admission and severe-morbidity risk differences are negative, while the all-cause-consultations risk difference is positive. This pattern does not by itself confirm or contradict the mortality result: secondary outcomes measure different events, and a difference in direction can reflect distinct underlying processes, measurement, or chance. Their estimates need to be read on their own definitions and scales.

The secondary outcomes are relevant context because they describe other aspects of health and service use during the stated timeframe. However, they are not equivalent to the primary endpoint and should not be combined into a single conclusion. Each result has its own uncertainty, and the comparisons are unadjusted. The registry record does not report a procedure to control the overall false-positive risk across the collection of secondary outcomes or other analyses.

Unadjusted secondary findings carry less inferential weight when many outcomes are examined, because some apparently notable results can arise by chance even when there is no underlying difference. This concern does not mean a secondary result is necessarily false; it means the result needs cautious interpretation and ideally confirmation in a prespecified analysis. The record does not report which secondary comparisons were prespecified in the statistical plan, whether all planned secondary outcomes were analyzed, or whether any additional analyses were conducted. They should therefore be treated as supportive descriptive evidence rather than as independent confirmation of the primary result.

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

• Non-accidental Hospital Admission
• Severe Morbidity
• All-cause Consultations
• Mid-upper-arm Circumference
• Weight-for-age Z-score
• BCG Scarring
• Cost-effectiveness Analysis of Providing BCG at Home-visits
• Cause Specific Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the observed counts from the uncertainty and assumptions surrounding their comparison. The endpoint is binary at the participant level: each participant is counted as having or not having the event during the defined follow-up. The arm counts therefore describe participants with an event, not the total number of events if one participant could experience repeated events. The registry record specifies the outcome unit as participants.

What does the risk difference describe?

A risk difference compares the event proportions between two groups by subtracting one group's proportion from the other's. It is expressed on an absolute scale, so its value describes the size and direction of the difference in event probability rather than a relative multiple. For the primary endpoint, the posted risk difference is -0.016. The negative sign indicates that the recorded event proportion was lower in the intervention arm than in the control arm. This is a statistical description of the observed groups, not a statement about what would happen to every individual.

The comparison also reports a risk ratio and an odds ratio. A risk ratio compares the event proportions as a ratio; an odds ratio compares the odds of the event. These relative measures answer different questions from an absolute risk difference, and their numerical magnitudes are not interchangeable. The primary risk ratio is 0.300, with interval endpoints 0.132 and 0.683. The odds ratio is 0.295, with interval endpoints 0.128 and 0.678. The registry record does not report the confidence level for these intervals. Each measure depends on the same underlying outcome data but presents the contrast on a different scale.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.002. In general, a p-value describes how surprising data at least as incompatible with a specified null model would be if that model and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. Because this value is unadjusted, it does not reflect correction for examining multiple endpoints or analyses. The registry record does not report a multiplicity strategy.

Why does randomization matter?

In general, random assignment is intended to make treatment groups comparable in expectation with respect to both measured and unmeasured characteristics. That rationale depends on the assignment process being implemented as planned and on appropriate handling of participants after assignment. The record identifies the study as randomized but does not report how the sequence was generated or concealed. It also does not describe a detailed analysis population or missing-data procedure. The posted arm comparison should therefore be interpreted alongside those reporting gaps rather than assuming details that are not recorded.

Why do follow-up and outcome definitions matter?

The primary endpoint has specific start and stop rules. Participants entered the analysis at enrolment or 24 hours of age, whichever came later. Follow-up ended at the earliest of the listed subsequent visit, a registered non-trial vaccine, death, migration, or 60 days of life. Such rules define which time at risk contributes to the comparison. A participant who stops being followed earlier does not have the same observed follow-up as one who remains under observation through the full timeframe. The record does not report how incomplete outcome ascertainment was handled, so it is not possible to assess that issue from the posted description alone.

The record lists a count-based outcome, not a time-to-event estimate. A count comparison does not directly show when events occurred or account explicitly for differing follow-up durations in the way a time-to-event analysis might. The posted summary should therefore be understood in the context of the specified follow-up rules and not as a rate per unit of person-time. The record does not report a separate time-to-event analysis for the primary outcome.

What does an interval estimate add?

In general, an interval estimate conveys uncertainty around a point estimate under a statistical method and its assumptions. A narrower interval indicates greater precision for that method; a wider one indicates less precision. It does not include every source of uncertainty, such as bias from outcome classification or missing data. For the primary risk difference, the posted interval extends from -0.026 to -0.006. The interval's endpoints describe the range, while the point estimate gives the central estimate. Since the confidence level is not reported in the registry record, it should not be assigned a level by assumption.

The posted p-value, point estimate, and interval are related aspects of the same unadjusted comparison. They should be considered together with the outcome definition, arm counts, and limitations of the record. A small p-value does not eliminate uncertainty about the magnitude, generalizability, bias, or completeness of the evidence.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.016, with an interval from -0.026 to -0.006. This interval expresses uncertainty around the absolute comparison under the calculation method used. Its two endpoints are negative, as is the point estimate. The registry record does not report the confidence level or enough methodological detail to identify all assumptions behind the interval.

Other measures describe the same primary comparison on relative scales. The risk ratio is 0.300, with interval endpoints 0.132 and 0.683; the odds ratio is 0.295, with interval endpoints 0.128 and 0.678. These relative measures should not be read as absolute changes. Because the event is uncommon in the posted groups, absolute and relative summaries can give different intuitive impressions of the contrast. The arm counts and risk difference help retain the absolute scale.

Precision is not the same as validity. An interval may quantify sampling uncertainty under its method, but it cannot show whether outcome ascertainment was complete, whether the analysis followed a prespecified plan, or whether the comparison is affected by bias. The registry record does not report missing-data methods, an adjustment strategy, or the confidence level. These omissions constrain how fully the posted interval can be evaluated.

The unadjusted p-value for the primary comparison is 0.002. It is not a substitute for the interval: the p-value addresses compatibility with a null model, while the interval conveys a range of estimates. Neither statistic measures the importance of the outcome to patients or determines whether the finding applies beyond the studied setting and follow-up period.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. The original design assumptions are not reported in the registry record. The stated planning method uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each planning scenario targets a stated fraction of the observed effect.

For these binary participant outcomes, the sample-size entries are participants per arm, not total participants across the trial. The planning rows describe detecting 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. The two power columns indicate the number of participants per arm estimated to be needed to have an 80% or 90% chance of detecting the specified effect under the stated assumptions, if that effect and those assumptions held. Higher target power generally requires more participants for the same effect.

The central planning lesson is that smaller effects need more participants to detect reliably. Thus, the entries for planning for 50% of the observed effect are larger than those for planning for the full observed effect. These estimates should not be interpreted as proof that the actual trial had a particular probability of detecting its result. This is not observed power.

Planning calculations use the observed effect as their starting point, so they are illustrative rather than independent evidence about the true effect. In particular, an observed effect may be imprecise, and a planning exercise that treats it as fixed does not capture all uncertainty about the effect. These figures help compare hypothetical design choices; they do not explain why the original trial enrolled its recorded number of participants.

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 = 0.023; treatment proportion p₁ = 0.007; average p̄ = 0.015.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1724 = 0.3379.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1720 = 0.1448.
4. n = (0.3379 + 0.1448)² / (-0.0163)² = 881.2, rounded up to 882 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 <- 0.0232172470978441                          # control proportion
p1 <- 0.00695825049701789                          # 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(2504203)
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 = 882 (80% power), 1,180 (90% power)
 75% of observed effect: n per arm = 1,776 (80% power), 2,376 (90% power)
 50% of observed effect: n per arm = 4,461 (80% power), 5,972 (90% power)
power.prop.test: 881.2 
Simulated power at n = 882 per arm: 0.831 (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 lists a primary endpoint and a set of secondary outcomes, but it does not report a multiplicity adjustment or a hierarchy for interpreting the outcomes. Multiplicity matters because testing several outcomes or comparisons can increase the chance of observing a small p-value by chance. The primary comparison's p-value is explicitly unadjusted, and the secondary comparison p-values are also presented as unadjusted. Their interpretation should account for the possibility of multiple testing rather than treating each result as if it were the only analysis.

The record does not report a detailed prespecified statistical analysis plan, including whether outcome definitions, analysis choices, or decision rules were finalized before results were examined. Nor does it report interim analyses or stopping rules for the trial. The status is listed as terminated, but the reason for termination and whether it was linked to an interim result are not reported in the registry record. No such explanation should be inferred from the status alone.

The primary population definition specifies when participants entered analysis and the events that ended follow-up. However, the record does not report an explicit intention-to-treat statement, per-protocol population, exclusions after randomization, missing-data method, imputation strategy, or sensitivity analysis. It is therefore not possible to establish from the registry record how participants with incomplete follow-up or missing outcome information were handled, or whether all randomized participants were retained in the reported comparison.

These reporting gaps do not negate the posted counts, but they limit assessment of robustness. A complete appraisal would benefit from the planned analysis details, outcome ascertainment procedures, handling of missing information, and an explanation of the terminated status. The record lists no separately reported analysis entries, while outcome comparison summaries are nevertheless posted; the distinction makes it especially important not to assume unreported analytical procedures.

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 and hospital admission (3.0%).

The registry record reports serious adverse events affecting 14 participants in the intervention arm, with 1006 at risk, and 36 participants in the control arm, with 1206 at risk. It separately records other adverse events affecting 3 among 887 at risk in the intervention arm and 0 among 1046 at risk in the control arm. Deaths are listed as 7 and 28, respectively. These are the posted counts; the record does not explain how the adverse-event categories relate to one another or whether they overlap, so the counts should not be added together.

The top serious-event term is “Mortality and Hospital Admission,” reported as 3.0%. The record does not give the denominator or additional detail for that term in the available summary. A serious-event count is not automatically a causal assessment: the reported numbers alone do not establish whether an event was caused by the intervention, and the registry record does not provide event-level narratives or attribution details.

Interpret these figures alongside the trial's follow-up definition and the endpoint counts, not as a complete safety profile. The record does not report enough information about event ascertainment, severity criteria, or attribution to support more detailed conclusions.

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

The posted primary data show fewer recorded non-accidental mortality events in the intervention arm than in the control arm during the defined follow-up period. The risk difference is -0.016, and its interval estimate ranges from -0.026 to -0.006. The unadjusted p-value is 0.002. These results describe the comparison recorded in this trial, with its specified participants, intervention, outcome definition, and follow-up limits.

They do not establish that every infant would experience the same outcome, nor do they show what would happen outside the trial's rural and urban settings or after the defined period. The result concerns BCG and OPV offered during home visits compared with no vaccines at those visits, with both arms described as receiving nursing care. It is not a comparison of every possible vaccination schedule or service-delivery approach.

The record identifies the trial as randomized, but it does not give full details of sequence generation, allocation concealment, outcome assessment, missing-data handling, or the statistical plan. It also does not report a reason for termination. Those gaps limit assessment of bias and robustness. A posted interval and p-value cannot resolve uncertainty caused by incomplete reporting or unmeasured sources of bias.

The secondary outcomes do not provide a single uniform pattern, and their tests are unadjusted. They offer context, not a replacement for the primary comparison or definitive confirmation. The serious-adverse-event summary also does not establish causal attribution. Taken together, the registry record supports a description of the posted mortality comparison, but it does not by itself support broader claims about all benefits, harms, mechanisms, or populations. No medical advice follows from these statistics alone.

17. Why This Trial Matters Statistically

This trial raises a statistical question about timing and delivery: whether offering vaccination through home visits shortly after birth is associated with a difference in early infant mortality under a particular follow-up definition. The randomized, parallel design makes a group comparison relevant, while the open-label designation and limited reporting of implementation details make careful assessment of outcome collection and analysis important.

The primary endpoint is a participant-level mortality outcome with explicit stopping rules. Those rules matter because follow-up does not necessarily continue for every participant through the same duration. Understanding the endpoint requires more than knowing the event count: the start point, censoring events, and 60-day limit define what the comparison means.

The record also illustrates why absolute and relative measures should be read together. The risk difference expresses an absolute contrast; the risk ratio and odds ratio express relative contrasts. Intervals add information about precision, while the unadjusted p-value addresses compatibility with a null model. None of these summaries can compensate for missing information about the analysis plan or missing outcomes.

Finally, the secondary-outcome set and the terminated status make transparency especially relevant. Without a reported multiplicity strategy, analysis plan, missing-data methods, or termination explanation, readers cannot fully distinguish planned inference from other possible analyses. The statistical importance of the trial lies not only in its primary estimate, but also in recognizing what the registry record does and does not document.

18. Limitations

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

Several limitations are specific to what is recorded for this trial. The registry status is terminated, but the reason is not reported. The record does not explain whether termination was administrative, operational, related to recruitment, or related to results. No explanation should be inferred.

The intervention description is incomplete after “Dependent on” and does not give the full details of the OPV component. It names two possible BCG formulations, but the available record does not clarify how the formulation was selected or distributed. This makes the intervention less fully specified in the record than would be ideal for assessing implementation and reproducibility.

The primary endpoint has several stopping events and a maximum timeframe of 60 days. The record does not report the amount of follow-up contributed by each participant or how incomplete follow-up was addressed. It also does not describe how non-accidental causes were classified, whether outcome assessors were masked, or how deaths and migration were ascertained.

Further limitations include no reported confidence level for the interval estimates, no detailed statistical plan, no multiplicity procedure, and no reported missing-data or sensitivity-analysis methods. The record identifies the study as randomized and unmasked but does not report sequence generation or allocation concealment. It also does not explain the serious-adverse-event attribution process. These are reporting limitations; they do not establish that the procedures were absent, only that they are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Can Earlier BCG Vaccination Reduce Early Infant Mortality? A Randomised Trial — NCT02504203.
• Registry record last updated 2026-05-26; status last verified 2026-02.
• Results first posted 2026-05-26.
• 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 phase 4, randomized, open-label, parallel trial sponsored by Bandim Health Project. Enrollment is listed as 2332; the start date is 2015-11, primary completion is 2021-06, and status is terminated.

The intervention was BCG and OPV at home visits shortly after birth, compared with no vaccines at home visits. The primary endpoint was non-accidental mortality through a follow-up period limited by specified events or 60 days of life. The posted counts were 7 among 1006 intervention-arm participants and 28 among 1206 control-arm participants. The unadjusted risk difference was -0.016, with an interval from -0.026 to -0.006 and an unadjusted p-value of 0.002.

Secondary comparison summaries are posted for hospital admission, severe morbidity, and all-cause consultations. Important analysis details, including the reason for termination, multiplicity handling, and missing-data procedures, are not reported in the registry record.