Safety and Efficacy of Hypothermia to Treat Neonatal Hypoxic-Ischemic Encephalopathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Hypothermia to Treat Neonatal Hypoxic-Ischemic Encephalopathy (NCT00890409), a randomized phase 3 study. The primary outcome is Death.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, phase 3 trial with no masking. Its official title identifies it as a multicenter randomized controlled trial in China. Fudan University is listed as the sponsor. The study status is completed, and the registry reports enrollment of 256 participants. The registry record does not report the number of study sites or the method used to generate or conceal the random allocation.

Participants were assigned to normothermia or hypothermia. The normothermia arm description specifies a rectal temperature target of 36.0-37.5 degree C. In the hypothermia arm, a cooling cap was fitted around the head for 72 hours. The cap temperature could be adjusted between 5 to 20 degree C, with an automatically regulated probe in the nasopharynx used to maintain a nasopharyngeal temperature of (34±0.2)degree C. The registry lists the cooling cap as a device intervention.

The primary endpoint was death by 18 months of age. The outcome results include 96 participants in the normothermia arm and 119 in the hypothermia arm. Those outcome denominators do not account for the full enrollment reported in the registry; the reason for the difference is not reported in the registry record. The record does not report the trial’s original sample-size justification or the assumptions used to design the study. The planning illustrations associated with the posted effect are not a substitute for the original design rationale.

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 Death, measured over 18 months.

The primary endpoint counts deaths by 18 months of age. It is a binary participant-level outcome: each participant either had the event during the stated follow-up period or did not. The registry describes the measure as the number of deaths, so the arm results are counts rather than a time-to-event estimate or a measure of the timing of death.

Death is a clinically important outcome that can be defined as an event without relying on a subjective rating scale. A fixed follow-up horizon also gives the outcome a clear time frame. However, a count at 18 months does not describe when deaths occurred, nor does it capture other aspects of health or development. The registry lists major adverse events as a secondary outcome, but detailed secondary results are not included in the posted information described in the record.

The endpoint is compared between randomized arms to assess whether their observed event experience differs. A difference in the observed counts alone is not enough to establish the size or certainty of a group difference, particularly when the arm denominators differ. The comparison estimate and its confidence interval provide information about the direction and precision of the between-arm contrast. The registry record does not report a more detailed endpoint definition, such as how deaths were ascertained or how participants without known outcome status were handled.

7. Results Posted in the Registry

• Hypothermia: 18.5% (22/119) versus 28.1% (27/96) on control; risk difference -9.6 percentage points (95% CI -21.0 to 1.7), risk ratio 0.66 (0.40–1.08); unadjusted two-proportion z-test p = 0.094.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a risk difference describe?

In general, a risk difference compares the proportion of participants with an event in one group with the proportion in another. A negative estimate for the hypothermia-versus-normothermia contrast means the observed event proportion was lower in the hypothermia arm. The estimate is a comparison of group outcomes, not a count of deaths prevented or a causal effect established by itself. The primary outcome is binary, so each participant contributes an event or a non-event to the relevant arm total.

The registry posts a risk-difference estimate and a confidence interval for the comparison. The point estimate gives the central value of the estimated contrast. The interval expresses uncertainty around that estimate under the statistical method used. Since the interval extends across zero, the results are compatible with no difference in event proportions. It also includes values on either side of zero, so the direction and size of a population contrast remain uncertain.

How should the p-value be understood?

In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test’s assumptions were correct. It is not the probability that the treatment has no effect, nor is it the chance that the result is due to chance. The registry reports an unadjusted p-value of 0.094 for the posted comparison. This value is above the conventional two-sided 0.05 threshold, but that threshold does not turn a result into proof of no difference when it is not crossed.

The registry record labels the posted comparison unadjusted. No adjusted estimate, covariate model, or detailed test specification is reported in the registry record. The method used for the sponsor’s original statistical analysis, if distinct from the posted calculation, is not reported in the registry record. The interpretation should therefore remain tied to the unadjusted result that is posted rather than assuming a particular model or adjustment strategy.

Why are counts and denominators both important?

Event counts show how many deaths were recorded in each arm, while denominators describe how many participants contribute to each arm’s outcome result. Counts without denominators can mislead when group sizes differ: the same count can represent different proportions in groups of different sizes. Here, both the count and the arm denominator are necessary context. The posted outcome comparison uses 96 participants in the normothermia arm and 119 in the hypothermia arm, while overall enrollment is 256. The record does not explain the difference between the enrollment total and these outcome denominators.

In general, a complete account of an endpoint would also state how outcome status was established, whether all randomized participants were included, how missing outcomes were handled, and what population was used for analysis. Those details are not reported in the registry record. Without them, readers cannot determine whether the endpoint counts represent all randomized participants or a defined subset, or how absent outcome information may have been treated.

What can randomization and lack of masking tell us?

In general, random allocation is intended to make the assigned groups comparable at the start of a trial, including with respect to characteristics that may not have been measured. It does not guarantee identical groups, and its value depends on how the sequence was generated, concealed, and implemented. The registry identifies the study as randomized but does not report those procedural details.

The registry lists masking as none. This means the record does not describe masked assignment. In general, knowledge of an assigned intervention can influence care, behavior, or outcome assessment, depending on the setting and outcome. Death is a more objective endpoint than many subjective outcomes, but the record does not describe how deaths were ascertained or whether outcome assessment had safeguards against bias. These are reporting limits, not evidence that bias occurred.

Why does over-dispersion matter in general?

Over-dispersion is a general issue for count outcomes when their variability exceeds what a chosen statistical model assumes. It can make standard errors too small and confidence intervals too narrow if the model does not account for the extra variability. It is not indicated as an issue for this primary endpoint: the registry classifies the outcome as participants with an event, rather than as a recurrent or continuous count outcome. The posted comparison is about whether a participant died by the specified follow-up time.

The registry also lists major adverse events as a secondary outcome, but it does not give detailed results or a full statistical plan for secondary outcomes. The record reports no analysis details for multiplicity, subgroup comparisons, interim analyses, or missing data. Those methods cannot be inferred from the fact that the study was randomized or from the posted primary comparison.

10. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated group contrast. The registry posts a confidence interval for the risk difference. In general, a confidence interval is a range of values compatible with the observed data under the interval’s statistical assumptions and method. It is not a guarantee that the true value lies within the range, nor does it show which values are clinically important.

For this outcome, the confidence interval extends from below zero to above zero. Zero represents no difference in event proportions between the arms. The interval therefore does not exclude no difference, and it allows for a contrast in either direction. The point estimate favors a lower observed event proportion in the hypothermia arm, but the interval indicates that the estimate is uncertain. The registry’s unadjusted p-value of 0.094 is consistent with that uncertainty and is above the conventional two-sided 0.05 threshold.

The record does not report the confidence interval method, any adjustment, or a prespecified threshold for a clinically meaningful difference. Precision should not be judged from the point estimate alone. The outcome denominators are 96 and 119, and the record does not explain why these do not account for the enrollment of 256. If outcome status was unavailable for some participants, the handling and potential implications are not reported in the registry record.

Thus, the posted interval gives a broad description of uncertainty, but the registry’s limited analysis details constrain how fully it can be evaluated. It does not establish equivalence between the groups, and it does not establish a difference. It indicates that this comparison does not precisely resolve whether the event proportions differed.

11. 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. Each row represents planning for a stated fraction of the observed effect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. Under the listed assumptions, the 80% power column gives the participants per arm for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding per-arm size for a 90% chance.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The registry’s original sample-size justification and design assumptions are not reported in the registry record. These figures are planning illustrations based on the observed result, not the study’s documented original enrollment target rationale.

For example, planning for 100% of the observed effect lists 301 participants per arm for 80% power and 403 participants per arm for 90% power. Planning for 75% of the observed effect lists 555 participants per arm for 80% power and 743 participants per arm for 90% power. Planning for 50% of the observed effect lists 1,291 participants per arm for 80% power and 1,727 participants per arm for 90% power. The curve conveys the same general relationship: smaller effects require more participants to detect under otherwise unchanged assumptions. These are planning illustrations, not observed power.

12. 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 = 0.281; treatment proportion p₁ = 0.185; average p̄ = 0.233.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5979 = 1.1719.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5940 = 0.4999.
4. n = (1.1719 + 0.4999)² / (-0.0964)² = 300.9, rounded up to 301 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 <- 0.28125                          # control proportion
p1 <- 0.184873949579832                          # 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(890409)
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 = 301 (80% power), 403 (90% power)
 75% of observed effect: n per arm = 555 (80% power), 743 (90% power)
 50% of observed effect: n per arm = 1,291 (80% power), 1,727 (90% power)
power.prop.test: 300.9 
Simulated power at n = 301 per arm: 0.802 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists death by 18 months as the primary outcome and major adverse events as a secondary outcome. It reports three outcome measures, but detailed definitions and results for the secondary outcome are not included in the information recorded. The record does not describe a multiplicity strategy, such as whether or how the statistical threshold was adjusted when assessing more than one outcome or analysis.

The registry reports no analyses. It does not describe interim analyses, subgroup analyses, or a hierarchy for interpreting multiple endpoints. Their use or absence cannot be inferred from the posted primary comparison. The registry record also does not report a complete statistical analysis plan, so it is not possible to determine which analyses were prespecified or whether the posted comparison follows the original plan.

Missing-data handling is not reported in the registry record. The outcome denominators are 96 in the normothermia arm and 119 in the hypothermia arm, whereas overall enrollment is 256. The record does not explain this difference, say whether all randomized participants had outcome status established, or state how participants with unknown status were handled. It also does not identify whether the primary analysis used an intention-to-treat population, a per-protocol population, or another analysis set.

These omissions matter because analysis populations and missing outcomes can affect the meaning of an arm comparison. They also limit assessment of whether the reported result is robust to alternative reasonable analysis choices. The available record does not establish that missingness or multiplicity altered the result; it simply does not provide the information needed to evaluate those questions.

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

The posted data show fewer deaths in the hypothermia arm by count, with 22 deaths among 119 participants, compared with 27 deaths among 96 participants in the normothermia arm. The unadjusted comparison estimate points toward a lower event proportion in the hypothermia arm. However, the confidence interval includes no difference, and the unadjusted p-value is 0.094. The result therefore does not provide a statistically conclusive distinction between the arms under the conventional two-sided 0.05 threshold.

This does not show that the groups are equivalent, nor does it prove that there is no difference. The uncertainty includes no difference and possible contrasts in either direction. Nor does the direction of the point estimate alone demonstrate that cooling caused a reduction in deaths. Interpretation depends on the randomized comparison, the conduct of the trial, outcome ascertainment, analysis population, and missing-data handling; key details on several of these points are not reported in the registry record.

The endpoint is limited to death by 18 months of age. It does not summarize other health or developmental outcomes, and the registry’s secondary outcome of major adverse events is not accompanied by detailed posted results in this record. Consequently, the primary comparison cannot by itself describe the overall balance of outcomes or harms.

The result is best read as an uncertain estimate from the posted trial data, not as a recommendation for care. The record supports describing the observed counts and their statistical uncertainty. It does not support a claim that the intervention works, does not work, or has a particular clinical benefit. The unexplained difference between overall enrollment and the outcome denominators further limits conclusions about the population represented by the primary result.

15. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read alongside its uncertainty, not only by comparing event counts. The hypothermia arm has fewer posted deaths by count, but the arm denominators differ, and the interval for the estimated risk difference includes zero. The unadjusted p-value of 0.094 does not meet the conventional two-sided 0.05 threshold. Together, these features make the result an example of a directional estimate that remains statistically uncertain.

The record also highlights the importance of participant flow and analysis populations. Enrollment is reported as 256, while the primary outcome denominators are 96 and 119. Without an explanation for that difference, readers cannot tell how the outcome analysis relates to all enrolled or randomized participants. Clear reporting of outcome availability and the analysis population would help assess how representative the posted comparison is.

Finally, the trial shows the difference between a result-based planning illustration and a trial’s original design rationale. The planning figures use fractions of the observed effect and specified assumptions, while the original sample-size justification is not reported in the registry record. That distinction prevents retrospective planning calculations from being mistaken for a documented design decision or for evidence about the trial’s power.

16. 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 trial-specific details needed to assess the result are not reported in the registry record. The method for sequence generation and allocation concealment is not described. Masking is listed as none, and the record does not explain how the primary outcome was ascertained. The number of centers is not reported, although the official title describes the study as multicenter.

Overall enrollment is 256, while the posted primary outcome denominators are 96 for normothermia and 119 for hypothermia. The record does not explain the difference, describe participant flow, or report the number with missing outcome status. It also does not state the analysis population or how missing outcomes were handled. These gaps restrict assessment of how the primary comparison relates to the enrolled trial population.

The registry does not report the original sample-size justification, a complete statistical analysis plan, or detailed analysis methods. It also does not provide detailed results for the listed secondary outcome of major adverse events. The primary endpoint captures death by 18 months but does not provide timing of death or other dimensions of outcome. The posted result is unadjusted, and the record does not report whether additional analyses were planned or conducted.

These limitations concern what can be evaluated from the registry record; they do not establish that the trial was conducted improperly or that any specific bias occurred. They do mean that the posted counts and comparison estimate should be interpreted with caution and that some questions about completeness and analysis cannot be resolved from the record.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: Safety and Efficacy of Hypothermia to Treat Neonatal Hypoxic-Ischemic Encephalopathy — NCT00890409.
• Registry record last updated 2009-05-28; status last verified 2009-05.
• Results first posted 2009-04-29.
• 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.

20. Record Summary

The registry record describes a completed, randomized, parallel-group, phase 3 trial of selective head cooling for neonatal hypoxic-ischemic encephalopathy. It lists Fudan University as sponsor, no masking, and enrollment of 256. The official title describes a multicenter randomized controlled trial in China.

The primary outcome was death by 18 months of age. The posted counts are 27 of 96 participants in the normothermia arm and 22 of 119 in the hypothermia arm. The unadjusted comparison has a risk-difference estimate in the direction of fewer events in the hypothermia arm, a confidence interval spanning zero, and a p-value of 0.094.

The registry lists major adverse events as a secondary outcome but does not report detailed secondary results. The original sample-size rationale, analysis populations, missing-data procedures, and explanation for the outcome denominators are not reported in the registry record.