Kangaroo Mother Care to Prevent Hypothermia in Term Infants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Kangaroo Mother Care to Prevent Hypothermia in Term Infants (NCT02189759), a randomized na study. The primary outcome is Number of Infants With Axillary Temperature <36.0 Degrees Celsius.

2. Clinical Question

3. Trial Design

The registry identifies NCT02189759 as a randomized, parallel-group trial with no masking. University of Alabama at Birmingham is listed as the sponsor. The record lists enrollment of 375 and a completed status. The start is recorded as 2014-08, with primary completion recorded as 2014-09.

Four intervention descriptions appear in the registry: continuous KMC and standard KMC, each specified either through one hour after birth or through discharge. The posted primary comparison is limited to the continuous and standard KMC groups specified through one hour after birth. Its arm records list 102 participants for continuous KMC and 101 for standard KMC. The record does not establish from these figures how the listed enrollment relates to the participants included in this particular comparison.

Both primary-comparison groups received, or were intended to receive, standard WHO thermoregulation care; continuous KMC was described as an addition to that care. The registry descriptions mention practices including warm delivery rooms, drying, breastfeeding, postponing bathing and weighing if needed, and appropriate bundling. Detailed operational instructions and the method used to generate or conceal the random allocation are not reported in the registry record. Masking is recorded as none.

The primary outcome is a participant count for axillary temperature below 36.0 degrees Celsius, measured from birth to one hour. The registry also lists neonatal intensive care unit admission and duration of KMC among secondary outcomes. The posted results include comparisons for duration of KMC, but a result for neonatal intensive care unit admission is not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Infants With Axillary Temperature <36.0 Degrees Celsius, measured over Time of birth to 1 hour.

The primary endpoint is the number of infants with an axillary temperature below 36.0 degrees Celsius from birth to one hour. Temperature was taken per axilla using a digital thermometer. This is a binary outcome at the participant level: an infant either meets the stated temperature threshold during the specified measurement period or does not. The posted group counts are 55 participants in the continuous-KMC group and 56 in the standard-KMC group.

Temperature is relevant to the trial's stated question because the registry describes prevention of neonatal hypothermia as the study's overall hypothesis. Its summary discusses moderate hypothermia, described as 32-36 degrees Celsius, and severe hypothermia, described as below 32.0 degrees Celsius. The posted primary endpoint uses the threshold below 36.0 degrees Celsius. These descriptions should be kept distinct: the reported endpoint is the stated participant count below its threshold, rather than a separately reported count for each severity category.

A participant count can be compared between groups as a difference in event risks, with the group denominators supplying the context for those counts. The endpoint provides a focused measure over the early period identified in the record. The registry does not report repeated temperature trajectories, additional measurement times, or a more detailed endpoint adjudication procedure.

7. Results Posted in the Registry

• Continuous Kangaroo Mother Care to One Hour After Birth: 53.9% (55/102) versus 55.4% (56/101) on control; risk difference -1.5 percentage points (95% CI -15.2 to 12.2), risk ratio 0.97 (0.76–1.25); unadjusted two-proportion z-test p = 0.827.

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.

Duration of Kangaroo Mother Care

• 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:
  • Continuous Kangaroo Mother Care to One Hour After Birth: mean 0.60 versus 0.00 on control; difference 0.60 (95% CI 0.11 to 1.09), standardized effect d = 0.34; z-test p = 0.016.
  • Continuous Kangaroo Mother Care to Discharge: mean 7.00 versus 0.00 on control; difference 7.00 (95% CI -0.84 to 14.84), standardized effect d = 0.29; z-test p = 0.080.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Continuous Kangaroo Mother Care to One Hour After Birth than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Continuous Kangaroo Mother Care to Discharge and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies neonatal intensive care unit admission and duration of KMC as secondary outcomes. Results posted for duration of KMC show a positive direction for the continuous-KMC comparisons, with more uncertainty in the comparison extending KMC through discharge than in the comparison through one hour. These secondary findings concern time spent in KMC, not the primary temperature endpoint, so they do not directly confirm or overturn the primary comparison.

A result for neonatal intensive care unit admission is not reported in the registry record. The available secondary results therefore do not cover every secondary outcome listed in the registry. Duration of KMC also reflects an intervention-related behavior rather than a clinical event identical to the primary outcome. A pattern across different outcomes can be informative about the trial's broader questions, but it should not be treated as a substitute for the prespecified primary endpoint.

The secondary comparisons are unadjusted. When several outcomes or contrasts are examined, some nominally notable results can arise by chance even if there is no underlying effect. Without a reported multiplicity plan, and with no reported analysis entries or full analysis plan, the secondary p-values carry less confirmatory weight than a single prespecified primary comparison would carry under a clearly documented analysis strategy. They are best considered exploratory evidence that needs interpretation alongside outcome definitions, precision, and the missing reporting details.

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

• Number Infants Admitted to the Neonatal Intensive Care Unit
• Duration of Kangaroo Mother Care

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared? The primary outcome is binary: the registry counts participants whose measured axillary temperature was below 36.0 degrees Celsius during the period from birth to one hour. The comparison uses the continuous-KMC group as the intervention group and the standard-KMC group as the comparator. The posted counts and denominators are 55 of 102 and 56 of 101, respectively. In general, comparing event risks accounts for the group sizes, whereas comparing counts alone would not.

How to read the risk difference? The posted risk difference is -0.015. It expresses the intervention-group event risk minus the comparator-group event risk on an absolute scale. A negative estimate points toward a lower observed event risk in the intervention group; a positive estimate would point in the other direction. The value is an estimate from the observed groups, not a guarantee of the underlying difference in a wider population. The registry also reports relative measures, the risk ratio and odds ratio. In general, absolute and relative measures describe different scales of association; neither by itself resolves uncertainty or establishes causation.

What does the confidence interval add? A confidence interval gives a range of estimates compatible with the observed data under the interval's statistical procedure. The posted interval for the risk difference is -0.152 to 0.122. Its span covers estimates in both directions, which is why the point estimate alone should not be treated as precise evidence about the direction of the group contrast. The registry does not state the interval construction method or confidence level, so those details are not reported in the registry record.

How should the p-value be read? The unadjusted p-value is 0.827. In general, a p-value describes how incompatible the observed data, or more extreme data, are with a specified null model under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not quantify the probability that the result will replicate. A large p-value does not establish that groups are equivalent. The test specification and any adjustment to the primary comparison are not reported in the registry record.

What can randomization contribute? Random allocation is intended to make comparison groups comparable, on average, with respect to measured and unmeasured factors at assignment. It does not ensure that groups are identical in a particular trial, and the benefit of randomization depends on appropriate allocation and analysis. The registry records randomization, but details of sequence generation, allocation concealment, adherence, and analysis population are not reported in the registry record. No masking is recorded, so participant and staff masking should not be assumed.

Why can outcome distributions matter? General statistical guidance is that the analysis should suit the outcome type and data distribution. For a binary outcome, a method may model risks, odds, or another specified quantity. For a continuous outcome, investigators may compare means, but skewed or highly variable observations can affect how well a simple model represents the data. Over-dispersion is a general concern when observed variability exceeds what a model assumes; it can make standard errors and intervals too small if ignored. The registry does not report enough detail to identify the methods underlying each posted estimate or to assess model checks.

The posted secondary comparisons use mean differences for duration of KMC, measured in hours, and include standard errors for the group means. Those comparisons have unadjusted p-values. In general, unadjusted tests do not account for the chance of false-positive findings when several outcomes or comparisons are examined. The registry does not report whether a multiplicity strategy was planned or applied. The primary comparison and secondary comparisons should therefore be interpreted according to their distinct outcome definitions and the level of analysis detail available.

The registry lists zero reported analysis entries and does not provide the trial's full statistical analysis plan. It is not possible to infer from the posted summaries whether analyses were prespecified, how missing observations were handled, whether the analysis followed assigned groups, or whether any interim review took place. Those procedures are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.015, and its confidence interval runs from -0.152 to 0.122. This interval is wide enough to include estimates below and above zero. Consequently, the data do not locate the group contrast precisely enough to settle whether the underlying event risk is lower or higher with continuous KMC during the stated period.

Precision concerns the range of values compatible with the observations and the statistical procedure; it is not the same as whether a result crosses a conventional significance threshold. The unadjusted p-value of 0.827 is consistent with the interval's broad uncertainty, but a p-value alone does not show how large or small plausible effects may be. The interval is more informative about the range of estimates than the point estimate alone, although its method and confidence level are not reported in the registry record.

The relative measures also have intervals that cover values on either side of no group difference: the risk ratio is 0.973 with interval 0.757 to 1.249, and the odds ratio is 0.940 with interval 0.541 to 1.634. These scales tell a similar broad story of uncertainty, but they are not interchangeable with the absolute risk difference.

The posted counts and intervals apply to the reported comparison, not necessarily to every participant listed under trial enrollment or every intervention group. Without reported missing-data handling, analysis-population definitions, or interval methods, it is not possible to determine whether additional analytic choices affect precision. The result should therefore be read as an uncertain estimate for the stated comparison rather than a precise measure of the effect in all term infants.

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 participants per arm, not total events. They use the observed primary risk difference as a reference and show planning for 100%, 75%, and 50% of that observed effect. For 100% of the observed effect, the estimates are 16,749 participants per arm for 80% power and 22,421 participants per arm for 90% power. For 75% of the observed effect, they are 29,754 and 39,831 participants per arm, respectively. For 50% of the observed effect, they are 66,896 and 89,554 participants per arm, respectively.

The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. In plain terms, the 80% column gives the planning size associated with an 80% chance of detecting the stated effect under those assumptions if that effect is real; the 90% column represents a higher target chance of detection. Smaller target effects require more participants because they are harder to distinguish from random variation.

These are planning illustrations calculated from the observed effect, not the original trial's design assumptions. The trial's own sample-size justification and design assumptions are not reported in the registry record. This is not observed power: it does not describe the probability that this completed trial detected its true effect.

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 = 0.554; treatment proportion p₁ = 0.539; average p̄ = 0.547.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7040 = 1.3798.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7039 = 0.5924.
4. n = (1.3798 + 0.5924)² / (-0.0152)² = 16,748.0, rounded up to 16,749 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 <- 0.554455445544555                          # control proportion
p1 <- 0.53921568627451                          # 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(2189759)
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 = 16,749 (80% power), 22,421 (90% power)
 75% of observed effect: n per arm = 29,754 (80% power), 39,831 (90% power)
 50% of observed effect: n per arm = 66,896 (80% power), 89,554 (90% power)
power.prop.test: 16748 
Simulated power at n = 16,749 per arm: 0.797 (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 reports no analysis entries and does not provide a detailed statistical analysis plan. It does not report whether the primary endpoint, comparison, or analysis method was prespecified in a protocol or finalized before outcome data were examined. The original sample-size assumptions and justification are also not reported in the registry record. The posted planning illustration based on the observed effect is not a substitute for that original design information.

Several interventions and outcomes are listed, and more than one comparison is posted for duration of KMC. The p-values for the posted comparisons are unadjusted. Whether the investigators planned to control the chance of false-positive findings across multiple outcomes or contrasts is not reported in the registry record. This matters particularly for secondary results: without a stated multiplicity strategy, they warrant more cautious interpretation than a single primary analysis.

The record does not report an intention-to-treat or per-protocol analysis population, how protocol deviations were handled, or how missing outcome measurements were addressed. The posted primary arm denominators are 102 and 101, but the record does not explain the relationship between those denominators, the listed enrollment of 375, and participants assigned to the other intervention groups. A reader cannot infer from the group counts alone whether all randomized participants were included in the analysis.

Interim analyses, stopping rules, allocation concealment, and methods for generating the random sequence are not reported in the registry record. The record lists no masking. These gaps do not prove that procedures were absent; they mean that the registry information does not permit their assessment. As a result, the estimates can be described as posted, but the analysis process and safeguards against bias or selective reporting remain unclear.

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

The posted primary result shows similar event counts in the two reported groups, with a risk-difference estimate of -0.015. Its confidence interval extends from -0.152 to 0.122, and the unadjusted p-value is 0.827. The interval includes both possible directions of difference, so the result does not precisely establish whether continuous KMC through one hour was associated with a lower or higher risk of an axillary temperature below 36.0 degrees Celsius in this comparison.

This finding does not demonstrate equivalence. An equivalence conclusion requires a defined margin and an analysis designed to assess whether plausible differences fall within that margin; neither is reported in the registry record. The result also does not establish that there is no effect. Rather, it describes an estimate with substantial uncertainty based on the posted groups and endpoint.

The primary endpoint is a temperature threshold measured during the period from birth to one hour. It is not a complete assessment of every aspect of thermoregulation, later temperature, neonatal intensive care admission, or other outcomes. The registry's broader hypothesis refers to moderate and severe hypothermia, but the posted primary comparison is the count below 36.0 degrees Celsius. Findings for one endpoint and time period should not be expanded to outcomes that were not reported.

The record describes continuous KMC through one hour and standard KMC through one hour as the primary contrast. It does not support conclusions about the versions continuing through discharge. No result for neonatal intensive care unit admission is reported in the registry record, and the adverse-event entries do not provide usable risk denominators. The evidence should therefore be read narrowly: it is an uncertain posted comparison for a specific early temperature outcome, not a general judgment about KMC or neonatal care.

16. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between a small point estimate and a precise estimate. The primary risk difference is close to zero, but its confidence interval is broad and extends in both directions. Looking only at the point estimate or p-value would omit important information about the range of effects still compatible with the data.

It also illustrates why the outcome definition and time window matter. The registry's hypothesis describes hypothermia categories, while the posted primary outcome counts participants below 36.0 degrees Celsius from birth to one hour. Clear separation of the motivating hypothesis from the operational endpoint helps readers understand precisely what was compared.

The record lists several intervention versions and secondary outcomes, but the posted primary result covers one specific pair of groups. This makes transparent reporting of the analysis population, missing observations, multiplicity strategy, and prespecified comparisons particularly important. Those details are not reported in the registry record, limiting assessment of how the posted estimates relate to the trial's full design.

Finally, planning estimates based on the observed effect can illustrate how sample-size requirements change with a target effect, but they do not recover the original design rationale or measure observed power. Keeping those concepts separate prevents a retrospective planning calculation from being mistaken for evidence about the trial's ability to detect its true effect.

17. Limitations

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

The primary result is posted for the continuous-versus-standard KMC comparison through one hour after birth, although the registry lists additional intervention versions that continue through discharge. Primary results for those other intervention groups are not reported in the registry record. The relationship between the listed enrollment of 375 and the denominators in the posted primary comparison is also not explained.

The primary endpoint is limited to axillary temperature below 36.0 degrees Celsius from birth to one hour. The registry does not report repeated measurements, later temperature outcomes, or further details about how readings were collected beyond the axillary digital-thermometer description. The reported endpoint should not be treated as a full account of later thermoregulation.

Details needed to assess analysis quality are missing, including the analysis population, missing-data handling, allocation concealment, and the statistical plan. The record gives no result for neonatal intensive care unit admission, despite listing it as a secondary outcome. The adverse-event entries record zero for the numbers at risk and affected in each listed group; with no usable risk denominators, they do not allow a meaningful safety comparison.

Masking is recorded as none. The registry does not report whether outcome assessors were masked or whether that was feasible for temperature measurement. These reporting limits do not establish that trial procedures were inadequate, but they restrict what can be concluded from the registry record alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Kangaroo Mother Care to Prevent Hypothermia in Term Infants — NCT02189759.
• Registry record last updated 2017-06-19; status last verified 2017-04.
• Results first posted 2017-06-19.
• 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.

21. Record Summary

NCT02189759 is recorded as a completed randomized, unmasked, parallel-group trial sponsored by University of Alabama at Birmingham. The registry lists enrollment of 375 and compares several KMC intervention versions. The posted primary result concerns continuous versus standard KMC through one hour after birth.

The primary endpoint counts participants with axillary temperature below 36.0 degrees Celsius from birth to one hour. The groups recorded 55 of 102 and 56 of 101 participants, respectively. The risk-difference estimate is -0.015, with confidence interval -0.152 to 0.122 and unadjusted p-value 0.827, leaving substantial uncertainty about the direction and size of the contrast.

Duration of KMC is reported as a secondary outcome, while a result for neonatal intensive care unit admission is not reported in the registry record. The analysis plan, missing-data procedures, and original sample-size justification are not reported.