Kangaroo Mother Care Before Stabilisation Amongst Low Birth Weight Neonates in Africa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Kangaroo Mother Care Before Stabilisation Amongst Low Birth Weight Neonates in Africa (NCT02811432), a randomized na study. The primary outcome is Mortality Within 7 Days.

2. Clinical Question

3. Trial Design

This was a randomised, controlled trial with two parallel groups. The registry lists the allocation as randomised and the masking as none, so the trial was open label. The intervention group was allocated kangaroo mother care, and the control group was allocated standard care. The registry describes the study as a multi-site trial conducted at four hospitals in Uganda.

The recorded enrollment was 2221. The intervention is described as skin-to-skin care initiated as soon as possible following randomisation; standard care is described as an incubator or radiant warmer. The primary outcome was mortality within 7 days. Other listed outcomes include hypothermia at 24 hours, time to clinical stabilisation, time from starting procedures to death, hospital stay, feeding at discharge, mortality within 28 days, readmission, and weight gain at 28 days.

The registry record lists the study status as completed, with a start date of 2019-10-13 and a primary completion date of 2022-09-30. The sponsor is the London School of Hygiene and Tropical Medicine. The trial's original sample-size justification, planned interim analyses, and detailed analysis plan are not reported in the registry record. The enrollment figure should not be confused with the denominator used for every outcome: posted denominators differ across outcomes, and the registry gives outcome-specific group counts.

Because masking was none, allocation was known to participants and trial staff. In general, this can matter especially for outcomes involving care procedures or clinical judgement. Mortality is a comparatively concrete endpoint, but the registry information alone does not establish how outcome ascertainment or other potential sources of bias were handled.

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 Mortality Within 7 Days, measured over 7 days.

The primary endpoint was mortality within 7 days, reported as the count of participants with the event. It measures whether a participant died during the specified early follow-up period. The posted results give 81 events among 1083 participants in the intervention group and 83 among 1102 participants in the control group.

In general, a primary endpoint gives a trial a central outcome around which the main comparison is organised. Defining the main question in advance can help distinguish the principal analysis from the many other outcomes that may be measured. Mortality is also an event that can be counted directly, unlike outcomes that require rating, interpretation, or repeated measurement. However, an endpoint's importance does not by itself resolve questions about how completely outcomes were observed or how missing observations were handled.

The timeframe matters: this endpoint concerns deaths within 7 days, not mortality over a longer period. The registry lists mortality within 28 days as a secondary outcome, which addresses a different follow-up window. The primary result therefore speaks specifically to the recorded comparison within the first 7 days. It does not, by itself, describe longer-term outcomes or the full course of neonatal care.

The registry summary states that the trial hypothesised a 25% overall reduction in mortality within 7 days. That is the trial's stated expectation, not a description of the observed effect. The posted primary comparison should instead be read through its estimated risk difference, uncertainty interval, and p-value.

7. Results Posted in the Registry

• Intervention: 7.5% (81/1083) versus 7.5% (83/1102) on control; risk difference -0.1 percentage points (95% CI -2.3 to 2.2), risk ratio 0.99 (0.74–1.33); unadjusted two-proportion z-test p = 0.963.

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.

Prevalence of Hypothermia at 24 Hours Post-randomisation

• 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: 40.9% (448/1096) versus 53.1% (585/1101) on control; risk difference -12.3 percentage points (95% CI -16.4 to -8.1), risk ratio 0.77 (0.70–0.84); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Duration of Hospital Stay in Days

• 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 errors.
• Result:
  • Intervention: mean 7.30 versus 6.10 on control; difference 1.20 (95% CI 0.80 to 1.60), standardized effect d = 0.25; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Proportion of Neonates Exclusively Breastmilk Feeding at Discharge

• 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: 88.6% (959/1083) versus 88.7% (978/1102) on control; risk difference -0.2 percentage points (95% CI -2.9 to 2.5), risk ratio 1.00 (0.97–1.03); unadjusted two-proportion z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results cover several different types of outcome, including hypothermia, hospital stay, feeding at discharge, and other outcomes listed in the registry. Their overall pattern is not identical to the primary mortality result: some posted secondary comparisons are more distinct from zero than the primary comparison, while others are not. These outcomes address different aspects of care and follow-up, so they should not be treated as interchangeable measures of the same effect.

In particular, secondary findings do not overturn or replace the primary mortality comparison. A difference in a secondary outcome can coexist with an uncertain primary result because outcomes measure different events, use different timeframes, and may have different patterns of missingness or measurement. The registry lists mortality within 28 days separately from the primary mortality endpoint within 7 days; one timeframe cannot be used as a direct substitute for the other.

The secondary p-values are unadjusted. In general, testing multiple outcomes without a stated multiplicity strategy increases the chance that at least one comparison will appear statistically notable by chance. This does not mean that a secondary finding is necessarily false; it means the strength of evidence is lower when the number of comparisons and their prespecification are unclear. The registry record does not report a testing hierarchy or multiplicity adjustment.

It is also important not to over-generalise from the subset of secondary results with posted estimates. The record lists more outcomes than it supplies detailed comparison results for, and the registry does not report analyses for every listed measure. Overall, secondary outcomes can add context about patterns across different endpoints, but they are best treated as supportive and hypothesis-generating unless a prespecified analysis plan gives them a stronger confirmatory role.

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

• Prevalence of Hypothermia at 24 Hours Post-randomisation
• Time From Intervention/Control Procedures Starting to Clinical Stabilisation
• Time From Starting Intervention/Control Procedures to Death
• Mean Duration of Hospital Stay in Days
• Proportion of Neonates Exclusively Breastmilk Feeding at Discharge
• Mortality Within 28 Days
• Frequency of Readmission
• Daily Weight Gain at 28 Days

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either had the recorded event within the specified timeframe or did not. In general, a risk difference expresses the difference between the event proportions in two groups. A value near zero corresponds to similar observed risks; a negative value indicates a lower event proportion in the intervention group than in the control group. The posted estimate is -0.001. This is an unadjusted contrast based on the posted group summaries.

A confidence interval gives a range of values reasonably compatible with the data under the method's assumptions. It is not a range containing a fixed proportion of individual outcomes, and it is not a probability statement that the true effect lies in that particular interval. For the primary endpoint, the reported interval runs from -0.023 to 0.022. Because it includes zero and extends in both directions, it does not rule out either a lower or a higher event risk in the intervention group. The interval should be considered with the point estimate, rather than treating the point estimate as exact.

The p-value for the primary comparison is 0.963. In general, a p-value assesses how unusual data at least as incompatible with a null hypothesis would be if that hypothesis and the statistical model were correct. It is not a direct measure of effect size, clinical importance, or the probability that a treatment effect exists. A large p-value does not demonstrate that the groups are identical. The confidence interval provides more direct information about the range of effect estimates compatible with the data.

For binary outcomes, event counts and denominators are essential context. The registry posts the primary outcome counts separately by group, and the denominator is not identical for every outcome. Missing or unavailable outcome observations can affect interpretation, but the registry record does not report how missing data were handled, how many outcomes were missing for each participant, or whether the analysis used a particular analysis population. These details should not be inferred from the counts alone.

The registry also reports a mean difference for hospital stay. In general, a difference between group means describes the contrast in average outcome values, while a standard error describes uncertainty in estimating a mean. The posted group means are 7.3 days for the intervention group and 6.1 days for the control group; the reported mean difference is 1.2 days, with a p-value of <0.001. The group summaries list standard errors of 0.15 and 0.14. A mean comparison can be sensitive to the shape of the outcome distribution and to unusually high or low values. The registry record does not report the distribution of hospital stay or the detailed analysis used.

In general, over-dispersion matters when outcome variability is greater than the statistical model assumes. A model that understates variability can produce confidence intervals that are too narrow and p-values that are too small. The registry does not report a model-based analysis for the primary endpoint, nor does it report a dispersion estimate for that endpoint. The binary primary outcome is presented as counts, a risk difference, and a confidence interval; further modelling details are not reported in the registry record.

The randomized allocation is intended to support a comparison of groups formed without systematic selection into intervention or control. Randomisation does not guarantee that all baseline characteristics are identical, especially in an individual trial, and the registry excerpt does not give baseline balance information. Masking is listed as none. In general, lack of masking can affect behaviour, co-interventions, assessment, and recording, depending on the outcome and trial procedures. The record does not describe safeguards or procedures to address these possibilities.

The posted p-values are labelled unadjusted. In general, an unadjusted p-value evaluates a comparison without accounting for the number of other comparisons being examined. When many secondary outcomes are tested, the chance of at least one small p-value under a collection of null effects increases. That is why secondary findings typically need a prespecified testing strategy and cautious interpretation. The registry record lists no reported analyses and does not state a multiplicity adjustment or hierarchy for secondary outcomes.

The registry record does not report the original sample-size justification, the planned significance level for the primary trial analysis, planned interim analyses, or a full statistical analysis plan. Planning illustrations based on observed effects are not a substitute for those original design details. They serve a different purpose: they show how assumed effect size and stated planning assumptions relate to illustrative sample requirements, not what the trial originally planned or achieved.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.001, and its confidence interval extends from -0.023 to 0.022. This interval includes zero and values on either side of it. The data therefore do not pinpoint a single effect value: they remain compatible with a range of possible group differences. The point estimate is close to zero, but uncertainty around it should not be ignored.

In general, precision describes how narrowly an estimate is determined by the data and statistical method. A confidence interval that spans a broad set of plausible effects conveys less precision than a narrower one. An interval crossing zero does not prove there is no effect; it indicates that the data do not distinguish a zero difference from some differences in either direction at the interval's stated confidence level. The registry excerpt does not specify the confidence level, so no level should be assumed from the record alone.

The p-value of 0.963 is consistent with the interval's inclusion of zero, but it answers a different question and should not replace the interval when considering the range of effects compatible with the data. Likewise, the counts alone do not describe precision: the uncertainty interval is necessary for understanding how much the estimate could vary under the analysis method.

Precision also depends on the outcome and the observed data. The primary mortality endpoint is distinct from the secondary outcomes, and their intervals cannot be used as a substitute for the primary interval. The registry record does not report missing-data handling, the analysis population, or detailed modelling choices that could affect uncertainty. These omissions limit assessment of whether the reported interval captures all relevant sources of uncertainty.

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 of sample requirements under specified assumptions, not a reconstruction of the trial's original design. The registry record does not report the original sample-size justification or its design assumptions. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

For the non-time-to-event outcomes, the planning figures are participants per arm. Time-to-event planning figures, if shown, are total numbers of events using the Schoenfeld approach. The distinction matters: a per-arm participant count is not the total across both groups, whereas an event target for a time-to-event analysis is expressed as a total event count.

The 80% power column represents the illustrative number of participants per arm needed for an 80% chance of detecting the specified effect under the assumptions, if that effect were the true effect and the analysis conditions held. The 90% power column applies the same idea with a higher target chance of detection. Greater target power generally requires more participants for a given assumed effect. The rows that plan for 75% or 50% of the observed effect assume smaller differences to detect than the row based on 100% of the observed effect; smaller effects need more participants to distinguish from random variation.

These are planning illustrations, not observed power. They do not describe the probability that the completed trial found a real effect, and they do not establish whether the original trial was adequately planned. In particular, the observed effect is itself uncertain, so using it as the basis for a planning illustration does not turn it into a known or stable design target. The figures should be read as conditional examples under the stated assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.075; treatment proportion p₁ = 0.075; average p̄ = 0.075.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3726 = 0.7303.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3726 = 0.3136.
4. n = (0.7303 + 0.3136)² / (-0.0005)² = 3,948,368.7, rounded up to 3,948,369 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 <- 0.0753176043557169                          # control proportion
p1 <- 0.074792243767313                          # 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(2811432)
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 = 3,948,369 (80% power), 5,285,745 (90% power)
 75% of observed effect: n per arm = 7,024,966 (80% power), 9,404,436 (90% power)
 50% of observed effect: n per arm = 15,818,869 (80% power), 21,176,977 (90% power)
power.prop.test: 3948369 
Simulated power at n = 3,948,369 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

Multiplicity arises when a study evaluates several endpoints or carries out several statistical comparisons. Even when each individual test is conducted at a conventional threshold, examining many tests increases the chance of at least one apparently notable result occurring by chance. The registry lists numerous secondary outcomes, including outcomes related to hypothermia, time to stabilisation, hospital stay, feeding, mortality within 28 days, readmission, and weight gain. The registry record does not report a multiplicity adjustment, a hierarchy of endpoints, or which secondary outcomes were intended to support confirmatory conclusions.

The listed secondary p-values are unadjusted. They should therefore be read as outcome-specific comparisons, not as if they accounted for all the other tests. The registry record also lists no reported analyses. It does not report whether outcomes were selected or grouped in advance for particular statistical tests, nor whether any secondary analyses were exploratory.

Missing-data procedures and analysis populations are also not reported in the registry record. The posted denominators vary by outcome, but the record does not explain why they differ, whether missing observations occurred, how they were handled, or whether participants were analysed according to their assigned groups. It is therefore not possible to assess from the registry information whether the analyses used an intention-to-treat population, a per-protocol population, or another defined population.

The record does not report planned interim analyses or a detailed statistical analysis plan. These omissions leave important aspects of the intended inference unclear, including any prespecified multiplicity control and the handling of incomplete outcome data. They do not establish that such procedures were absent from trial conduct; they establish only that they are not reported in the registry record. As a result, the strongest interpretation should remain tied to the posted estimates, their uncertainty, and the limits of the information recorded.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: saes and other adverse events (6.0%), neonatal infections (3.3%), neurological disorders (0.9%), neonatal jaundice (0.6%), hyperthermia (0.2%).

The registry reports serious adverse event figures for 1051 participants at risk in each group. Serious adverse events affected 124 participants in the intervention group and 125 in the control group. It separately reports other adverse events affecting 180 participants in the intervention group and 90 in the control group. Deaths are listed as 119 and 134, respectively. These are posted counts, and the registry record does not give a comparison estimate or uncertainty interval for them.

The registry lists serious-event terms including “SAEs and other adverse events” at 6.0%, neonatal infections at 3.3%, neurological disorders at 0.9%, neonatal jaundice at 0.6%, hyperthermia at 0.2%, and acute kidney injury at 0.1%. These terms and figures describe the adverse-event information recorded in the registry; they do not by themselves establish a causal relationship with group allocation.

In general, safety counts are interpreted in light of definitions, observation periods, completeness of reporting, and the way events were attributed and grouped. Those details are not reported in the registry record. The counts should therefore be read as descriptive information, not as a complete comparative safety analysis or a basis for medical advice.

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

The primary result describes a randomised comparison of mortality within 7 days between neonates allocated to kangaroo mother care and those allocated to standard care. The posted estimate is close to zero, and the confidence interval includes zero and differences in either direction. The primary data therefore do not establish a clear group difference for this endpoint. They also do not establish that the groups are equivalent or that any possible effect is exactly zero.

The trial's stated hypothesis was a 25% overall reduction in mortality within 7 days. The registry's posted primary comparison does not demonstrate that hypothesised reduction. At the same time, the interval leaves a range of possible differences compatible with the data, so the result should not be recast as proof that a meaningful difference is impossible. The conclusion is limited by the precision of the estimate and the information available in the registry record.

The result applies to the specific endpoint and population described: low birth weight neonates at four hospitals in Uganda, with the primary endpoint defined within 7 days. It does not answer every question about longer-term mortality, hospital care, or other outcomes. Secondary endpoints can contribute context, but their unadjusted comparisons have less evidential weight when multiplicity procedures and the analysis plan are not reported.

The record also does not report important details needed for a fuller assessment, including missing-data methods, the analysis population, the original sample-size justification, and interim analyses. The absence of those details from the registry record should not be interpreted as proof that the procedures were not conducted. It does mean that the posted results cannot be assessed against those methodological details using registry information alone.

Nothing in the statistical comparison alone determines what care should be given to an individual neonate. The findings describe group-level evidence from this trial and should not be translated into medical advice or a claim that one care approach works or does not work.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate, confidence interval, and p-value should be read together. The mortality estimate is close to zero, but the interval includes differences in both directions. The p-value is not a measure of the probability that the intervention has no effect, and the absence of a clear statistical difference does not demonstrate equivalence. Precision determines how narrowly the comparison has been estimated.

It also shows the distinction between a primary question and a collection of secondary questions. A trial may report outcomes spanning mortality, temperature, feeding, hospital stay, and other aspects of care. Those outcomes can be informative, but each answers a distinct question. Without a reported multiplicity plan, unadjusted secondary findings warrant more caution than a prespecified primary comparison.

The registry further demonstrates the value of reporting denominators, endpoint definitions, and analysis plans. The outcome-specific participant counts are useful context, but the reasons for differing denominators and the handling of missing observations are not reported. A detailed statistical analysis plan would help readers understand which populations, methods, and comparisons were intended before outcome results were available.

Finally, planning illustrations based on observed effects answer a different question from the trial's original sample-size calculation. They can show how sample requirements change as the target effect becomes smaller, but they do not reveal what assumptions guided the trial or whether its design matched those assumptions. Separating planning illustrations from observed evidence is essential for sound interpretation.

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.

The registry record does not report the original sample-size justification, so the enrollment cannot be evaluated against the trial's intended effect size, power target, or design assumptions. The planning illustrations based on observed effects are not a substitute for that information. Planned interim analyses and a full statistical analysis plan are also not reported.

Details about missing data and analysis populations are not reported. The outcome-specific denominators differ, but the registry record does not explain the reasons or describe how incomplete observations were treated. It is also not possible to determine from the record whether participants were analysed according to assigned groups or under another population definition.

The trial was open label, as the registry lists masking as none. The record does not describe how outcome assessment, clinical decisions, or event reporting were conducted in light of that design. The registry also does not provide baseline balance information in the registry record presented for the results, so the posted outcome comparison cannot be assessed alongside those characteristics.

The primary result concerns mortality within 7 days only. Other listed outcomes use different timeframes or measure different events. Some outcomes listed in the registry do not have posted detailed comparisons in the available results, and the registry lists no reported analyses. The secondary comparisons that are posted are unadjusted, while a multiplicity strategy is not reported.

Finally, the adverse-event record gives counts and selected event terms, but does not report a comparative analysis, uncertainty estimates, attribution procedures, or detailed observation rules. These limitations concern the information reported in the registry record; they do not prove that additional methods or procedures were not used during the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Kangaroo Mother Care Before Stabilisation Amongst Low Birth Weight Neonates in Africa — NCT02811432.
• Registry record last updated 2026-01-08; status last verified 2023-09.
• Results first posted 2026-01-08.
• 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 OMWaNA study, NCT02811432, was a completed randomised, open-label, parallel-group trial sponsored by the London School of Hygiene and Tropical Medicine. It compared kangaroo mother care initiated as soon as possible following randomisation with standard care described as an incubator or radiant warmer. The registry records enrollment of 2221 and describes the study as conducted at four hospitals in Uganda.

The primary endpoint was mortality within 7 days. The posted counts were 81 among 1083 intervention participants and 83 among 1102 control participants. The risk-difference estimate was -0.001, with a confidence interval from -0.023 to 0.022 and an unadjusted p-value of 0.963. The interval includes zero and extends in both directions, so the posted data do not establish a clear difference in this primary endpoint.

The registry lists secondary outcomes and adverse-event counts, but does not report a full analysis plan, missing-data methods, the original sample-size justification, or a multiplicity strategy. Those limits should be kept in view when interpreting secondary findings and the scope of the posted results.