Effects of Hypothermia Upon Outcomes After Acute Traumatic Brain Injury: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Hypothermia Upon Outcomes After Acute Traumatic Brain Injury (NCT00178711), a randomized phase 3 study. The primary outcome is The Dichotomized Glasgow Outcome Scale.

2. Clinical Question

The outcome assessment was planned at six months, with a window of plus or minus one month, and was performed in person by examiners blinded to treatment group. The stated primary question is therefore about a patient-centered functional outcome at a defined follow-up time, rather than an intermediate measure of temperature control or brain physiology. The registry’s brief summary frames the hypothesis as an increased number of favorable outcomes in the hypothermia group compared with normothermia. The posted primary outcome, however, is expressed as the number of participants with a poor outcome, so the direction of the outcome coding matters when interpreting the estimate.

The registry record gives a randomized comparison and an intention-to-treat outcome population, but it does not report a detailed account of how every randomized participant contributed to the primary outcome analysis. The record also does not report the original sample-size justification or the intended statistical analysis plan. These omissions limit assessment of whether the posted analysis follows the complete prespecified approach. The registry record is the basis for describing the question and results; it does not establish additional details about trial conduct beyond what is recorded.

3. Trial Design

NCT00178711 is a phase 3 randomized, double-masked, parallel-group trial titled Effects of Hypothermia Upon Outcomes After Acute Traumatic Brain Injury. The sponsor is The University of Texas Health Science Center, Houston. The registry lists a start date of 2005-11, primary completion in 2009-12, and trial status as terminated. Enrollment is listed as 232. These registry descriptors identify the intended design and status but do not, by themselves, explain why the trial was terminated or how termination affected follow-up and analysis; that information is not reported in the registry record.

Participants were assigned to hypothermia or normothermia. The hypothermia arm description specifies moderate hypothermia to 33 degrees Celsius, achieved within 2.5 hours of injury and maintained for 48 hours. The brief summary gives a related but not identical timing description: induction to < 35˚C by < 2.5 hours after severe traumatic brain injury and reaching 33˚C by 4 hours. These descriptions are reported as written and should not be treated as a single additional protocol detail beyond the registry’s wording. The control arm is described as treated at normothermia. The intervention is categorized as a device.

Random allocation supports a comparison between assigned groups, while double masking is intended to reduce the influence of treatment knowledge on relevant aspects of trial conduct and assessment. The primary outcome description specifically says that the examiners were blinded to treatment group. The registry does not provide further details of the masking procedures, how allocation was generated or concealed, adherence to the temperature strategy, or the handling of crossovers. Those details are not reported in the registry record.

The primary outcome was assessed in person at six months after injury, with a window of plus or minus one month. The posted primary population is intention to treat. The outcome arm counts are 52 for hypothermia and 45 for control, whereas total enrollment is listed as 232. The registry record does not explain the relationship between those arm counts and total enrollment in sufficient detail to reconstruct participant flow or establish the reasons for the difference. It also does not report the trial’s own original design assumptions, planned interim analyses, or a full protocol-level analysis plan.

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.

Before assignment: Enrollment criteria at the first eligibility assessment were ages 16-45, non-penetrating brain injury, and not responsive to instructions. 232 participants met these criteria and also had none of a first set of exclusion criteria. At the second eligibility assessment, 97 patients had none of a second set of exclusion criteria.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention to Treat

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.

Population: hypothermia group-- 26 ± 9 years of age, 40 males/12 females normothermia group--31 ± 11 year of age, 41 males/4 females

6. Primary Endpoint

The registry lists the primary outcome as The Dichotomized Glasgow Outcome Scale, measured over 6 months with a window of plus or minus one month.

The primary endpoint is the dichotomized Glasgow Outcome Scale at six months after injury, assessed in person within a window of plus or minus one month. The scale is divided into two outcome categories for this analysis. Good recovery and moderate disability count as favorable outcomes. Severe disability, a vegetative state, and death count as poor outcomes. The registry reports the endpoint as the number of participants with a poor outcome and identifies the analysis population as intention to treat.

Dichotomization turns a graded functional outcome into a binary classification. In general, a binary endpoint can make the comparison easier to express as the number of participants who meet a defined outcome criterion in each group. The trade-off is that distinctions within each category are not preserved: participants with good recovery and moderate disability are both classed as favorable, while severe disability, vegetative state, and death are grouped as poor. The endpoint therefore answers a focused question about the frequency of poor status, not about every difference in function or the full ordering of outcomes.

Functional status is relevant to the stated trial question because the registry asks whether outcomes after traumatic brain injury differ by randomized treatment group. Assessment at six months provides a specified follow-up point, and blinded examiners are intended to limit influence from knowledge of assignment during assessment. The registry record does not report additional psychometric details or an explanation for selecting this particular dichotomy. The posted outcome counts should be read according to the stated poor-outcome definition, rather than as counts of favorable outcomes.

7. Results Posted in the Registry

• Hypothermia: 59.6% (31/52) versus 55.6% (25/45) on control; risk difference 4.1 percentage points (95% CI -15.7 to 23.8), risk ratio 1.07 (0.76–1.51); unadjusted two-proportion z-test p = 0.686.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the risk ratio represent?

The sponsor reports a risk ratio for the poor-outcome category. In general, a risk ratio compares the probability of an event in one group with the probability in a reference group. A value of 1 represents equal event risks; values above or below 1 indicate that the event is more or less frequent in the numerator group, respectively. Because the event is a poor outcome, the interpretation must retain that outcome definition. The reported value of 1.08 is a point estimate, not a count and not a statement that treatment caused an outcome.

The sponsor’s reported method is logistic regression, while the reported effect measure is a risk ratio. The registry does not describe the model specification, covariates, or method used to derive that measure from the regression. It is therefore not possible to determine from the registry record whether the result is adjusted for other variables or how any adjustment was carried out. The reported estimate should be presented as recorded, without inventing model details.

What does the confidence interval add?

In general, a confidence interval represents a range of effect estimates that are reasonably compatible with the data and the statistical model at the stated confidence level. The sponsor’s 95% interval runs from 0.76 to 1.53. Because it includes 1, it is compatible with no relative difference as well as with effects in either direction. Its width signals that the result is imprecise: the data do not pin down a narrow range of relative effects. A confidence interval does not assign a probability to the true effect being inside its particular endpoints.

For the recalculation, a risk difference is also available. In general, a risk difference expresses the absolute contrast between event risks in the groups, whereas a risk ratio expresses a relative contrast. The two measures answer related but distinct questions, and their numerical scales differ. The recalculated risk-difference interval includes zero, its no-difference value. The recalculation is explicitly a simple, unadjusted calculation from the posted summary statistics; it is not a substitute for the sponsor’s own analysis.

Why distinguish the sponsor analysis from the recalculation?

The sponsor analysis is the trial’s reported statistical result. The recalculation uses the posted counts and group sizes to obtain a straightforward unadjusted comparison. Such a recalculation can help readers understand how the summary counts relate to an effect measure, but it may not reproduce the original model or any features of the planned analysis. The registry does not supply enough model detail to reconstruct the sponsor’s logistic regression. The sponsor’s reported risk ratio, confidence interval, and p-value should therefore remain distinct from the recalculated estimates and p-value.

The posted sponsor result is risk ratio 1.08, 95% confidence interval 0.76 to 1.53, p = 0.67. The recalculated unadjusted p-value is 0.686. The registry data do not mark a discrepancy between these analyses. A p-value is not an estimate of the size of an effect: it reflects the data under a null model and the assumptions of the test. The effect estimate and confidence interval are needed to describe direction and precision.

What is the role of the binary endpoint?

The primary Glasgow Outcome Scale endpoint classifies participants into favorable and poor categories. In general, analyzing a binary endpoint compares event occurrence rather than retaining every level of an ordered or graded scale. This can make interpretation direct when the clinical question concerns a prespecified category, but it also discards information about differences within categories. The posted count is for poor outcome; it should not be confused with the count of favorable outcomes. The registry describes the endpoint categories but does not report alternative primary analyses using the full scale.

Counts and denominators are essential to interpretation. The hypothermia arm has 31 poor outcomes among 52 participants, and control has 25 among 45. The sponsor’s result reports the relative effect, while the recalculation also gives an absolute effect measure. Neither should be interpreted without noting that the listed outcome arm counts are smaller than the total enrollment listed in the registry. The reason for this difference and the detailed participant flow are not reported in the registry record.

What do power and sample-size calculations mean?

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios use the observed effect and fractions of that effect. In general, power is the probability that a specified study design would reject a null hypothesis under a particular assumed effect, if the model assumptions hold. The 80% and 90% columns show the participants per arm indicated by the planning calculation for those power targets. They are not observed power and do not describe the probability that the trial’s result is true.

The illustrations show the planning consequences of targeting smaller effects: smaller effects require more participants to detect under the same assumptions. These figures are not evidence that the trial was designed with those assumptions, because the original sample-size justification and planning assumptions are not reported in the registry record. The sample-size assumptions for the illustration are known, but they must not be attributed to the trial’s investigators as original protocol choices.

What does over-dispersion mean in general?

Over-dispersion is a general statistical concern when observed variability is greater than a model expects. For binary outcomes, extra variability can arise when participants or observations are more heterogeneous than assumed, or when outcomes are correlated within groups. If a model ignores relevant extra variability, standard errors may be too small and confidence intervals may be too narrow. This is a general explanation, not a claim that over-dispersion occurred in this trial. The registry record does not report an over-dispersion assessment or the model diagnostics needed to evaluate one.

Likewise, the registry record does not report interim analyses, a formal multiplicity strategy, detailed missing-data procedures, or a full statistical analysis plan. These omissions should not be filled in by assuming standard practice. The posted information supports description of the endpoint, counts, and reported model, but not reconstruction of unreported analysis decisions.

10. Confidence Intervals and Precision

The sponsor’s risk-ratio estimate is 1.08, with a 95% confidence interval from 0.76 to 1.53. The interval includes 1, the no-relative-difference value, and spans values on either side of it. This means the estimate is not precise enough to rule out either a lower or a higher relative risk of poor outcome in the hypothermia group. The point estimate alone should not be treated as a conclusive description of the underlying effect.

In general, a confidence interval reflects both the observed data and the assumptions of the statistical model. A narrower interval indicates greater precision about the estimated effect; a wider interval indicates greater uncertainty. The interval is not a range containing 95% of individual participant outcomes, and it is not a probability statement that the true effect lies within the reported endpoints. Its interpretation is conditional on the analysis and its assumptions.

The recalculated absolute risk-difference interval also includes zero, its no-difference value. This reinforces that the posted summary statistics are compatible with no absolute difference as well as differences in either direction. The recalculated interval and the sponsor’s relative-effect interval use different scales, so their endpoints should not be compared directly. The sponsor’s analysis remains the trial’s reported analysis; the recalculation is an unadjusted descriptive check based on the summary counts.

Precision is also relevant to the trial’s listed enrollment and outcome counts. The registry lists enrollment of 232, while the outcome arms contain 52 and 45 participants. The record does not explain the relationship between those values or provide enough detail to assess the effect of missing outcome data. The uncertainty in the effect estimate is visible in the confidence interval, but the record’s limited participant-flow and missing-data information prevents a fuller evaluation of how the available outcome data may relate to all randomized participants.

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 sample-size figures are planning illustrations expressed as participants per arm, not total events. They use the observed effect as a reference and show scenarios for planning to detect 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. Under each scenario, the displayed columns correspond to planning for 80% power and 90% power. In plain terms, the figures indicate how many participants per arm the calculation suggests would be needed to have the stated chance of detecting the assumed effect, if the assumptions of the calculation apply.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The registry record does not report the trial’s original sample-size justification or its own design assumptions. These planning figures therefore illustrate the implications of selected effect assumptions; they should not be interpreted as the study’s actual planned enrollment target.

The scenarios make the effect-size trade-off visible: smaller effects require more participants per arm to detect at the same power target under the same assumptions. The listed values are 2,326 and 3,113 participants per arm for planning for 100% of the observed effect; 4,147 and 5,552 for planning for 75% of the observed effect; and 9,359 and 12,528 for planning for 50% of the observed effect. Within each pair, the first figure is for 80% power and the second is for 90% power. These are planning illustrations, not observed power.

The curve should be read as another view of how required sample size changes with the effect targeted under the calculation’s assumptions. It is not a record of participants enrolled or a forecast of the trial’s result. The calculations do not establish whether the original trial was adequately planned, because the protocol’s original sample-size assumptions are not reported in the registry record.

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 = 0.556; treatment proportion p₁ = 0.596; average p̄ = 0.576.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6989 = 1.3699.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6983 = 0.5877.
4. n = (1.3699 + 0.5877)² / (0.0406)² = 2,325.0, rounded up to 2,326 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 <- 0.555555555555556                          # control proportion
p1 <- 0.596153846153846                          # 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(178711)
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 = 2,326 (80% power), 3,113 (90% power)
 75% of observed effect: n per arm = 4,147 (80% power), 5,552 (90% power)
 50% of observed effect: n per arm = 9,359 (80% power), 12,528 (90% power)
power.prop.test: 2325 
Simulated power at n = 2,326 per arm: 0.800 (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. Analyses Reported by the Sponsor

The sponsor’s own reported analysis is a logistic regression analysis expressed as a risk ratio. It gives a risk ratio of 1.08, a 95% confidence interval from 0.76 to 1.53, and p = 0.67. The registry does not report additional details about the regression model, such as its covariates or the method used to obtain the risk ratio.

The unadjusted recalculation uses the posted arm counts and group sizes. It gives an unadjusted p-value of 0.686 and effect estimates with confidence intervals that include the respective no-difference values. This is a simple recalculation, not a reconstruction of the sponsor’s regression model. The two analyses are not marked as discrepant in the registry data, but they should be described according to their different methods and sources.

The sponsor’s analysis is the result to use when describing the trial’s own reported statistical analysis. The recalculation can help relate the arm counts to simple unadjusted contrasts, but it does not replace the reported result. The registry record does not provide enough information to assess whether the sponsor analysis included adjustments or other prespecified features.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one posted analysis and zero posted secondary outcomes. It does not report a multiplicity adjustment strategy or describe whether additional analyses were planned but not posted. Multiplicity arises in general when several hypotheses or outcomes are tested: the chance of at least one false-positive finding can increase as the number of tests grows. This is a general consideration, not evidence that multiple testing occurred in this trial. The recorded outcome and analysis count do not establish the full set of analyses conducted.

The primary outcome population is identified as intention to treat. In general, an intention-to-treat approach analyzes participants according to their randomized assignment, regardless of treatment received, and is intended to preserve the benefits of randomization. However, the registry record does not provide a detailed account of how this population was implemented for the posted outcome analysis. The posted arm counts are 52 for hypothermia and 45 for control, while total enrollment is 232. The record does not explain this difference, provide a complete participant flow, or state how participants without an observed primary outcome were handled.

Missing-data procedures are not reported in the registry record. There is no description of imputation, assumptions about missing outcomes, sensitivity analyses, or the amount and pattern of missing primary outcome data. Without those details, it is not possible to assess from the registry record whether missingness may have affected the comparison or how robust the result is to alternative assumptions.

The original statistical analysis plan, interim analyses, and the trial’s original sample-size assumptions are also not reported in the registry record. No claim can therefore be made about whether interim monitoring occurred, whether a stopping rule was used, or whether the posted analysis matches a prespecified protocol. These are reporting gaps, not proof that the relevant procedures were absent. The interpretation should remain anchored to the endpoint, arm counts, and sponsor analysis that are posted, while treating unreported design and analysis details as unknown.

15. Safety Results

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

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: decreased cerebral perfusion pressure (40.4%), elevated intracranial pressure (26.9%), blood stream infection (4.5%), acute respiratory distress syndrome (4.4%), pulmonary embolism (3.8%).

The serious adverse event figures are organized by groups described as randomized to hypothermia and hypothermia maintained, randomized to normothermia and normothermia maintained, randomized to hypothermia and then excluded, and randomized to normothermia then excluded. The corresponding numbers at risk are 52, 45, 67, and 68. The serious adverse event counts are 30, 20, 11, and 5, respectively. The other adverse event counts are 42, 38, 22, and 30, respectively. These are registry counts within the stated groups; they should not be read as a treatment effect estimate or as evidence that an event was caused by the assigned intervention.

The registry also lists serious adverse event terms, including Decreased Cerebral Perfusion Pressure at 40.4%, Elevated Intracranial Pressure at 26.9%, Blood Stream Infection at 4.5%, Acute Respiratory Distress Syndrome at 4.4%, Pulmonary Embolism at 3.8%, and Subdural Hemorrhage at 2.2%. The record does not provide enough detail alongside these terms to establish all denominators, overlap between events, or how the terms relate to the group-level counts. The percentages should therefore be understood as reported rather than used to reconstruct additional totals.

Death counts are not reported in the registry record’s adverse-event summary. The excluded-group labels indicate that those groups were excluded, but the reasons and timing are not reported in the registry record. The figures describe the posted safety data and do not by themselves establish comparative safety or causation.

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

The central statistical result is the sponsor-reported risk ratio of 1.08 for poor outcome, with a 95% confidence interval from 0.76 to 1.53 and p = 0.67. The interval includes the no-relative-difference value and permits estimates in either direction. The posted outcome counts are 31 poor outcomes among 52 participants in the hypothermia arm and 25 among 45 in control. Together, these data describe an uncertain estimate rather than a precise separation between the groups.

The result does not demonstrate that the strategies are equivalent. A non-significant p-value is not a test of equivalence, and the registry does not report an equivalence or non-inferiority objective or margin. Nor does the estimate prove that one strategy improves or worsens outcomes. The confidence interval is broad, and the posted analysis does not tightly determine the direction or magnitude of the relative effect.

The endpoint is specifically the dichotomized Glasgow Outcome Scale at six months, with poor outcome defined as severe disability, a vegetative state, or death. The findings do not describe every dimension of recovery, the full distribution of Glasgow Outcome Scale categories, outcomes at other times, or effects in populations beyond the registry’s stated population. The record identifies people aged 16–45 with severe traumatic brain injury in the summary, so broader application is not established by this result alone.

The trial is listed as terminated, but the reason is not reported in the registry record. The available data do not explain whether termination affected enrollment, follow-up, or the precision of the estimate. The outcome arm counts are smaller than total enrollment, and the record does not provide a full explanation of participant flow or missing outcomes. Those limitations should be kept in view when describing the posted finding.

In general, the most defensible interpretation is that the registry reports an imprecise comparison for the specified poor-outcome endpoint, with no clear separation from the no-difference value in the sponsor’s analysis. This statistical description is not medical advice and does not determine how an individual should be treated. It is limited to the recorded endpoint and analysis.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be interpreted together with its confidence interval. The sponsor’s risk-ratio estimate is 1.08, but its 95% confidence interval extends from 0.76 to 1.53. A point estimate gives one summary of the observed comparison; the interval shows that the data are compatible with a substantially broader range of relative effects. Reporting only the point estimate or p-value would obscure that uncertainty.

The endpoint also makes clear how outcome definition shapes interpretation. The primary measure is a dichotomized Glasgow Outcome Scale, and the posted event counts are for poor outcome, not favorable outcome. Stating which category is counted prevents the common mistake of treating a larger event count as automatically favorable. The division into favorable and poor categories makes the question direct, while grouping different levels of disability and recovery means that the result does not retain all the scale’s detail.

The comparison between the sponsor’s regression result and the simple unadjusted recalculation shows why analysis methods should be identified rather than blended together. The recalculation can provide a transparent check from the counts, while the sponsor’s analysis is the trial’s own reported estimate. Without model details, the posted result cannot be fully reconstructed from the registry record.

Finally, the distinction between observed results and planning illustrations is important. The sample-size figures describe hypothetical planning under stated assumptions, not what the trial’s original investigators planned and not observed power. Smaller effects require more participants in those illustrations, emphasizing how limited enrollment and imprecise estimates can constrain what a study can resolve. The original design assumptions and the reasons for termination are not reported in the registry record, so the illustrations cannot answer whether the trial’s original design was adequate.

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 leaves several trial-specific uncertainties. It lists enrollment of 232, but the primary outcome arm counts are 52 and 45. The relationship between these values is not explained, and a complete account of participant flow, exclusions, follow-up, and outcome availability is not reported in the registry record. This makes it difficult to assess how representative the posted outcome data are of all randomized participants.

The primary population is identified as intention to treat, but the registry does not describe in detail how missing outcomes were handled or whether all randomized participants were included in the analysis. Missing-data amounts, reasons, assumptions, and sensitivity analyses are not reported. These gaps limit assessment of potential bias from incomplete outcome information.

The trial is listed as terminated. The reason for termination and its timing or impact on recruitment and follow-up are not reported in the registry record. The original sample-size justification, statistical analysis plan, interim analyses, allocation procedures, masking procedures beyond the stated double masking and blinded outcome examiners, and model details are also not reported. These omissions prevent a full audit of whether the posted analysis followed the planned analysis.

The intervention timing is described in two ways in the record: the brief summary states induction to < 35˚C by < 2.5 hours and reaching 33˚C by 4 hours, while the arm description says 33 degrees Celsius was achieved within 2.5 hours and maintained for 48 hours. The registry wording does not explain this difference. The safety summary also includes groups labeled as excluded, without reporting the reasons for exclusion, and death counts are not reported in that summary.

These limitations do not invalidate the posted estimate, but they constrain how completely it can be evaluated. The interpretation should remain specific to the recorded endpoint and reported analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effects of Hypothermia Upon Outcomes After Acute Traumatic Brain Injury — NCT00178711.
• Registry record last updated 2014-09-17; status last verified 2014-09.
• Results first posted 2014-08-11.
• 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

NCT00178711 is a phase 3 randomized, double-masked, parallel-group trial of hypothermia versus normothermia after severe traumatic brain injury. The registry lists enrollment of 232, status as terminated, and a primary completion date of 2009-12. The primary endpoint was poor status on the dichotomized Glasgow Outcome Scale at six months after injury, assessed in person by examiners blinded to treatment group.

The posted outcome counts are 31 of 52 in the hypothermia arm and 25 of 45 in control. The sponsor reported a risk ratio of 1.08, 95% confidence interval 0.76 to 1.53, p = 0.67. The interval includes the no-difference value and indicates an imprecise comparison. The registry does not report the reason for termination, the original sample-size assumptions, or detailed missing-data and analysis-plan information.