TOBY (TOtal Body hYpothermia): a Study of Treatment for Perinatal Asphyxia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TOBY (TOtal Body hYpothermia): a Study of Treatment for Perinatal Asphyxia (NCT00147030), a randomized na study. The primary outcome is Combined Incidence of Mortality and Severe Neurodevelopmental Disability in Survivors.

2. Clinical Question

The registry states the hypothesis that prolonged whole body cooling could reduce death and severe neurodevelopmental disability. The primary outcome combines mortality with severe disability among survivors, so it addresses survival and severe developmental outcome as a single endpoint. The posted results give the number of participants with the combined outcome in each arm and an unadjusted comparison. They do not, by themselves, show how the outcome’s components contributed separately to the combined count. Component-specific primary outcome results are not reported in the registry record.

The study was randomized, with parallel arms and no masking. Its stated aim was to determine whether cooling to 33-34°C was safe and improved survival without severe neurological or neurodevelopmental impairments at 18 months. The registry record does not report further detail about eligibility criteria, outcome assessment procedures, or the planned statistical analysis.

3. Trial Design

TOBY (TOtal Body hYpothermia) is a completed randomized, parallel-arm trial sponsored by Imperial College London. The registry lists an enrollment of 325 and records the study start as 2002-12 and primary completion as 2006-11. The phase is listed as NA. Masking is listed as none, meaning the registry describes the trial as open-label rather than masked.

One arm received whole body mild induced hypothermia in addition to standard intensive care. Cooling was intended to continue for 72 hours, beginning by 6 hours of age, followed by rewarming at a maximum rate of 0.5 degree C per hour to normothermia. The comparator arm received standard intensive care. The registry identifies the intervention as a procedure.

The primary outcome was the combined incidence of mortality and severe neurodevelopmental disability in survivors at 18 months. The registry also lists secondary outcomes involving intracranial haemorrhage, persistent hypotension, pulmonary haemorrhage, pulmonary hypertension, prolonged blood coagulation time, culture proven sepsis, necrotising enterocolitis, and cardiac arrhythmia. Twenty-two outcome measures are listed overall, while 21 secondary outcomes are posted.

Random allocation supports a comparison between the assigned groups because, in expectation, it balances both measured and unmeasured characteristics. In an open-label trial, participants and clinical teams know the assigned treatment. That knowledge can affect care or assessment, depending on the outcome and how it is measured. The registry does not report masking of outcome assessors or details of allocation concealment. The original protocol, planned analysis populations, and trial-specific sample-size justification are 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.

Before assignment: 494 infants were assessed for eligibility; 94 did not meet inclusion criteria, 30 declined to participate 45 were not enrolled for other reasons. 325 underwent randomization.

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.

Population: Infants who were less than 6 hours of age who had a gestational age of at least 36 weeks and perinatal asphyxial encephalopathy confirmed by 30 minutes' amplitude-integrated electro-encephalography that showed abnormal background activity or seizures.

6. Primary Endpoint

The registry lists the primary outcome as Combined Incidence of Mortality and Severe Neurodevelopmental Disability in Survivors, measured over 18 months.

The primary endpoint counts participants who died or, if they survived, met the registry definition of severe neurodevelopmental disability at 18 months. Disability was defined by a score of less than 70 on the Mental Developmental Index of the Bayley Scales of Infant Development II (BSID-II), a score of 3 to 5 on the Gross Motor Function Classification System (GMFCS), or bilateral cortical visual impairment with no useful vision. The registry describes the BSID-II standardization mean as 100±15, with higher scores indicating better performance. GMFCS scores can range from 1 to 5, with higher scores indicating greater impairment.

This is a composite endpoint: different events are combined into one outcome. Combining death with severe disability among survivors makes the endpoint relevant to both survival and severe developmental status, while yielding a single comparison for the primary question. It also means that the overall result does not identify which component accounts for any difference between arms. A participant meeting more than one disability criterion still contributes to the combined endpoint as a participant with the outcome; the registry reports counts of participants, not counts of individual criteria met.

The primary outcome is reported as a number of participants, rather than as a mean score or time-to-event measure. The posted results count 74 participants in the cooled arm and 86 in the non-cooled arm. Separate component counts for mortality and each disability criterion are not reported in the registry record, so the combined endpoint should not be interpreted as if it were a disability-only measure or a mortality-only measure.

7. Results Posted in the Registry

• Non-cooled: 53.1% (86/162) versus 45.4% (74/163) on control; risk difference 7.7 percentage points (95% CI -3.2 to 18.5), risk ratio 1.17 (0.94–1.46); unadjusted two-proportion z-test p = 0.166.

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.

Intracranial Haemorrhage

• 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:
  • Non-cooled: 31.3% (21/67) versus 39.1% (25/64) on control; risk difference -7.7 percentage points (95% CI -24.0 to 8.6), risk ratio 0.80 (0.50–1.28); unadjusted two-proportion z-test p = 0.355.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-cooled and the control. The interval gives the range of effects that remain compatible with the data.

Persistent Hypotension

• 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:
  • Non-cooled: 82.7% (134/162) versus 77.3% (126/163) on control; risk difference 5.4 percentage points (95% CI -3.3 to 14.1), risk ratio 1.07 (0.96–1.19); unadjusted two-proportion z-test p = 0.222.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-cooled and the control. The interval gives the range of effects that remain compatible with the data.

Pulmonary Haemorrhage

• 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:
  • Non-cooled: 1.9% (3/162) versus 3.1% (5/163) on control; risk difference -1.2 percentage points (95% CI -4.6 to 2.1), risk ratio 0.60 (0.15–2.48); unadjusted two-proportion z-test p = 0.479.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-cooled and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover a range of neonatal complications during the hospital stay, with intracranial haemorrhage, persistent hypotension, and pulmonary haemorrhage among the outcomes with arm counts and unadjusted comparisons available. The directions of their point estimates are not uniform. Their reported intervals include the no-difference value, and their unadjusted p-values do not establish clear differences between the arms. The outcome-specific estimates are best understood as exploratory descriptions of the posted counts.

These results do not replace or alter the primary comparison. The primary endpoint asks about death or severe neurodevelopmental disability at 18 months, whereas the secondary outcomes concern other events, generally recorded during the hospital stay. They address different aspects of the trial and different time periods. The secondary findings cannot explain the primary composite result, particularly because component-specific primary outcome counts are not reported in the registry record.

Unadjusted secondary results carry less weight when many outcomes are examined. With multiple comparisons, the chance of finding an apparently notable result by random variation increases unless a suitable multiplicity strategy is used. The registry lists 22 outcome measures and 21 posted secondary outcomes, but no reported analyses or multiplicity adjustment. The statistical plan and any hierarchy among secondary outcomes are not reported in the registry record.

Accordingly, these secondary estimates should be treated as supportive context rather than independent confirmation of a treatment effect. They are also based on outcome-specific denominators, which can differ across measures. The registry does not report why denominators vary for every outcome or how missing observations were handled. No broad conclusion about all secondary outcomes should be inferred from a few posted comparisons, and absence of a clear difference in an unadjusted comparison is not proof that the groups were identical.

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

• Intracranial Haemorrhage
• Persistent Hypotension
• Pulmonary Haemorrhage
• Pulmonary Hypertension
• Prolonged Blood Coagulation Time
• Culture Proven Sepsis
• Necrotising Enterocolitis
• Cardiac Arrhythmia

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary comparison is between two randomized parallel arms: whole body cooling plus standard intensive care and standard intensive care alone. The endpoint is binary for each participant: the participant either had the combined outcome of death or severe neurodevelopmental disability at 18 months, or did not. For a binary outcome, the event count and the number assessed in each arm describe the observed frequency. The registry reports 74 of 163 in the cooled arm and 86 of 162 in the non-cooled arm.

The posted comparison expresses the contrast in several ways. The risk difference subtracts the observed event proportion in one arm from that in the other; its sign depends on the stated comparison order. The risk ratio compares the two event proportions as a ratio, while the odds ratio compares event odds. These measures are related but have different scales and interpretations. The risk difference is directly expressed on the event-proportion scale, whereas ratios express a relative comparison. None should be detached from its arm order or endpoint definition.

How should the interval and p-value be read?

A confidence interval gives a range of estimates compatible with the data and the method’s assumptions. A wider interval signals less precision; an interval that includes the no-difference value indicates that the data are compatible with no difference as well as with some effects in either direction. The primary risk-difference interval runs from -0.032 to 0.185. The risk-ratio and odds-ratio intervals also include their respective no-difference values. The registry does not identify the confidence level for these intervals, so no confidence percentage is assigned.

The unadjusted p-value of 0.166 summarizes the degree of incompatibility between the data and a no-difference null model, assuming the test’s conditions. It is not a measure of the size or clinical importance of an effect, and it does not state the probability that the null hypothesis is true. It also does not account for multiple comparisons unless an adjustment is applied; adjusted secondary analyses are not reported.

What does randomization contribute?

Randomization is intended to make the assigned groups comparable on average at the start of a trial, reducing systematic differences in baseline prognostic factors. It supports causal interpretation of an assignment-based comparison when allocation is implemented appropriately, outcomes are sufficiently complete, and the analysis follows an appropriate plan. The registry identifies the allocation as randomized but does not report the sequence-generation or concealment procedures, the analysis population, or the handling of non-adherence. Those details are not reported in the registry record.

Masking is listed as none. When treatment assignment is known, expectations or clinical decisions may influence care, reporting, or outcome assessment. Whether this affected the primary endpoint depends on the study procedures. The registry does not report whether outcome assessors were masked or provide enough detail to evaluate that possibility. The primary endpoint uses defined disability criteria, but a definition alone does not resolve all questions about ascertainment.

Why does the endpoint definition matter?

The primary endpoint combines mortality with severe neurodevelopmental disability among survivors. This can provide a single measure that captures two serious forms of outcome relevant to the trial’s stated question. The trade-off is that a composite can conceal different patterns across its components. A similar overall count could reflect different distributions of mortality and disability. The registry does not report separate primary component results, so the overall comparison cannot identify those patterns.

For a composite endpoint to be readily interpreted, its components should be understood in terms of their definitions and clinical meaning. Here, the disability definition includes a low BSID-II Mental Developmental Index, a specified GMFCS range, or bilateral cortical visual impairment with no useful vision. The registry provides the threshold descriptions but does not report the component counts or details of adjudication. Interpretations should therefore focus on the specified combined outcome, rather than inferring a result for any single component.

What is and is not reported about analysis?

The registry lists no reported analyses. The displayed comparison estimates are unadjusted re-calculations from the posted summary counts; they are not described as the trial’s own adjusted analysis. The discrepancy indicator is false, so no discrepancy between the posted counts and these re-calculations is flagged. The original statistical analysis plan, covariate adjustment, missing-data procedures, subgroup analyses, interim analyses, and analysis population are not reported in the registry record.

For binary outcomes, an unadjusted analysis treats the reported groups as the basis for comparison without accounting for covariates. This is transparent and can be checked against arm counts, but it may differ from a prespecified analysis that uses adjusted models or a particular population definition. No such sponsor analysis is posted in the registry record. Consequently, the unadjusted calculations are best read as a descriptive statistical comparison of the posted data, not as a substitute for an undocumented protocol analysis.

General statistical interpretation also depends on the process that generated the outcome data. Missing outcomes, changes in assigned treatment, and differences in follow-up can alter the meaning of a simple comparison. Their frequency and handling are not reported in the registry record. No claim about the size or direction of any such influence can be made from the available summary information.

11. Confidence Intervals and Precision

Precision is reflected by the range of values compatible with the observed data under the interval method. For the primary risk difference, the estimate is 0.077 and the reported interval extends from -0.032 to 0.185. That interval includes zero, the no-difference value for a risk difference. It therefore remains compatible with no difference and with effects in either direction. Its span also shows that the point estimate should not be treated as an exact value.

The relative measures convey a similar uncertainty. The risk ratio is 1.169, with an interval from 0.936 to 1.46; the odds ratio is 1.361, with an interval from 0.880 to 2.105. Each interval includes one, the no-difference value for a ratio. Across the measures, the observed direction is not estimated with enough precision to exclude no difference under these intervals. The registry does not report the confidence level, so these ranges are described without assigning a confidence percentage.

Precision depends partly on the amount of information in the data. Here the primary comparison has 163 participants in the cooled arm and 162 in the non-cooled arm, with the event counts reported as 74 and 86. The interval reflects sampling uncertainty under the calculation method; it does not capture all possible sources of uncertainty, such as measurement error, missing outcome data, or departures from the planned trial procedures.

A confidence interval is not a guarantee that the true effect lies within its limits, nor does an interval that crosses the no-difference value prove equivalence. A narrow estimate can still be affected by bias, while a wider interval may leave substantial uncertainty. The posted primary interval supports a cautious reading: the point estimate favors lower incidence in the cooled arm, but the data are also compatible with no difference and with a higher incidence in that arm. Further detail on the trial’s own analysis and missing data is not reported in the registry record.

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 for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the trial’s original design justification. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each planning row, the effect to detect is the stated fraction of the observed effect.

In plain terms, the 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions hold. The 90% column describes the corresponding target for a 90% chance. Higher target power generally requires more participants for the same effect. A smaller effect is harder to distinguish from random variation, so the planning figures rise as the assumed effect becomes a smaller fraction of the observed effect.

For the primary comparison, the figures are 663 participants per arm for 80% power and 887 for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 1,178 participants per arm for 80% power and 1,577 for 90% power. Planning for 50% of the observed effect gives 2,648 participants per arm for 80% power and 3,544 for 90% power. These are prospective planning illustrations rather than counts of participants enrolled in TOBY. They are not observed power.

Observed power is not a useful substitute for interpreting the estimate and its interval: after a study is complete, the estimate and precision describe the data more directly. The trial’s own sample-size assumptions and justification are not reported in the registry record. The planning figures should therefore not be read as evidence that the trial was designed around these assumptions, nor as a verdict on whether the trial was adequately planned.

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 = 0.454; treatment proportion p₁ = 0.531; average p̄ = 0.492.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7049 = 0.5933.
4. n = (1.3857 + 0.5933)² / (0.0769)² = 662.7, rounded up to 663 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 <- 0.45398773006135                          # control proportion
p1 <- 0.530864197530864                          # 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(147030)
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 = 663 (80% power), 887 (90% power)
 75% of observed effect: n per arm = 1,178 (80% power), 1,577 (90% power)
 50% of observed effect: n per arm = 2,648 (80% power), 3,544 (90% power)
power.prop.test: 662.7 
Simulated power at n = 663 per arm: 0.795 (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

Many outcomes or analyses create a multiplicity problem: the more comparisons considered, the greater the opportunity for chance patterns to appear. A prespecified primary endpoint helps focus interpretation, while secondary and exploratory outcomes generally require more cautious reading. The registry identifies a primary outcome and lists 22 outcome measures, with 21 secondary outcomes posted. It does not report a multiplicity adjustment, a testing hierarchy, or a statistical analysis plan. Those details are not reported in the registry record.

The registry lists zero reported analyses. The estimates discussed for the primary outcome and posted secondary outcomes are unadjusted re-calculations from the arm-level summary statistics, rather than reported sponsor analyses. The discrepancy indicator is false. The trial’s own inferential methods, any covariate adjustment, and any prespecified approach to secondary testing are not reported in the registry record. Unadjusted p-values should not be interpreted as if they account for the full family of outcomes.

Missing data can affect both the numerator and denominator in an outcome comparison. The registry gives arm denominators for the primary outcome, but it does not report a participant flow accounting, missing outcome counts, reasons for missingness, or a method for handling missing observations. The relationship between the enrolled population and the participants included in each analysis is not described. An intention-to-treat analysis, per-protocol analysis, or other analysis-population definition is not reported in the registry record.

Other important analysis details are also absent, including interim analyses, stopping rules, subgroup methods, and whether estimates were adjusted for baseline characteristics. No conclusions about these procedures should be inferred from the posted arm counts. These omissions limit the ability to assess whether the reported comparisons correspond to the original prespecified plan and how robust they are to alternative analytic choices.

These are reporting limitations, not evidence that particular procedures were or were not used. The registry record provides the outcome definitions and posted counts but does not provide enough analysis documentation to resolve the questions above. Interpretation should distinguish the transparent unadjusted comparisons from a complete evaluation of the trial’s statistical conduct.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardia arrhythmia (1.8%), hypotension (1.2%), major venous thrombosis not related to an infusion line. (1.2%), collapse (0.6%).

The registry lists serious adverse events among 163 participants at risk in the cooled group, with 8 affected, and among 162 participants at risk in the non-cooled group, with 3 affected. It also lists other adverse events affecting 126 participants in the cooled group and 134 in the non-cooled group, with the same respective numbers at risk. These are counts from the registry record; they should be read separately from the primary outcome comparison.

The most frequently listed serious adverse event terms are Cardia arrhythmia at 1.8%, Hypotension at 1.2%, Major venous thrombosis not related to an infusion line. at 1.2%, and Collapse at 0.6%. The registry does not provide event-specific counts by arm for these terms in the posted safety summary. Death counts in the safety groups are not reported in the registry record.

Adverse-event counts describe events recorded under the trial’s reporting procedures; they do not by themselves establish whether an event was caused by treatment. The registry does not report definitions, ascertainment details, severity grading beyond the serious-event grouping, or the full event-level data. These summary figures therefore provide limited descriptive safety information and do not support a complete safety assessment.

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

The posted primary comparison shows a higher observed count and incidence of the combined outcome in the non-cooled arm than in the cooled arm. The unadjusted risk-difference estimate is 0.077 in the non-cooled-versus-cooled direction. The reported interval extends from -0.032 to 0.185, and the unadjusted p-value is 0.166. Because the interval includes no difference, the estimate is imprecise with respect to the direction and size of the group contrast.

This result is not proof that the groups had the same outcome, and it is not proof that cooling changed the outcome. It is a comparison of the posted data with uncertainty. The point estimate is compatible with a lower observed incidence in the cooled arm, while the interval also permits no difference and effects in the opposite direction. The registry results alone do not establish the size of any underlying effect.

The endpoint combines mortality and severe neurodevelopmental disability among survivors at 18 months. It does not reveal separate results for mortality, BSID-II scores, GMFCS scores, or visual impairment. Those component-specific results are not reported in the registry record. Thus, the overall endpoint cannot be used to make a claim about any one component or about broader developmental outcomes not included in the definition.

The secondary comparisons and adverse-event summaries add context but do not settle the primary question. Secondary results are unadjusted, and the registry does not report a multiplicity plan. Safety counts are descriptive and do not establish causation. The registry also does not report missing-data handling, analysis populations, the full statistical plan, or the original sample-size justification.

The appropriate reading is therefore specific: the registry reports a randomized comparison of the assigned groups, an observed difference in the combined outcome, and intervals that include no difference. It does not provide enough detail to reconstruct every aspect of trial conduct or analysis, nor to turn the observed point estimate into a definitive claim about treatment effect.

17. Why This Trial Matters Statistically

TOBY poses a statistically challenging question because its primary outcome combines death with severe neurodevelopmental disability among survivors. The composite is designed to capture more than one important outcome in a single comparison, but it makes component-specific interpretation dependent on additional results. Without separate counts, readers cannot tell how mortality and disability contributed to the combined finding.

The randomized, parallel-arm design provides a framework for comparing the groups, while the open-label status and incomplete reporting of allocation and assessment procedures leave questions about implementation and outcome ascertainment. Those questions matter because a statistical estimate is only as interpretable as the data collection and analysis that generated it. The registry’s arm counts and unadjusted estimates are transparent, but they do not substitute for a protocol and analysis plan.

The primary interval includes the no-difference value and is compatible with estimates on either side of it. This illustrates why a point estimate should not be read alone. A single estimate can give a direction, while the interval indicates how much uncertainty remains. The trial therefore offers a useful example of distinguishing an observed contrast from a conclusive claim.

The secondary outcomes add another methodological lesson: multiple comparisons need context. A set of unadjusted results across many outcomes can generate patterns that are difficult to interpret without a prespecified hierarchy or multiplicity approach. The registry does not report those details, so secondary comparisons should remain descriptive.

Finally, planning illustrations based on an observed effect are not equivalent to original design assumptions. They can show how sample-size requirements change with effect size and power targets, but they cannot reveal what assumptions guided the trial. Keeping that distinction clear prevents retrospective calculations from being mistaken for the trial’s design record.

18. Limitations

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

Several limitations specific to the registry record affect interpretation. The primary outcome is a composite, but separate counts for mortality and the disability components are not reported. Readers cannot determine whether the overall group contrast reflects one component more than another. The registry also does not report the frequency of missing primary outcome data or the reasons for missingness.

The trial is described as randomized and unmasked, but sequence generation, allocation concealment, outcome assessor masking, treatment adherence, crossover, and participant flow are not reported in the registry record. These details are relevant to judging whether the posted comparison faithfully represents the randomized assignment and whether outcome measurement could have been influenced by knowledge of treatment.

The registry lists no reported analyses. The available comparison estimates are unadjusted re-calculations from summary statistics, and there is no posted statistical analysis plan to establish whether these match the prespecified primary analysis. Details of covariate adjustment, analysis populations, interim analyses, stopping rules, subgroup analyses, multiplicity control, and missing-data methods are not reported in the registry record.

Secondary results are also limited by the absence of a reported multiplicity strategy and by outcome-specific denominators. The posted summaries do not explain all denominator differences or provide enough event-level detail to evaluate ascertainment. Serious adverse event summaries lack arm-specific counts for individual terms, and deaths in the safety grouping are not reported.

These limitations concern what the registry record documents; they do not show that a particular trial procedure was absent or improperly conducted. They do mean that the posted summary cannot support a full audit of trial conduct, statistical analysis, or component-specific outcomes. Interpretations should remain confined to the counts and unadjusted comparisons that are reported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: TOBY (TOtal Body hYpothermia): a Study of Treatment for Perinatal Asphyxia — NCT00147030.
• Registry record last updated 2016-05-11; status last verified 2013-11.
• Results first posted 2016-05-11.
• 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

The registry describes TOBY as a completed randomized, parallel-arm trial with no masking and enrollment of 325. The sponsor is Imperial College London. The study compared whole body mild induced hypothermia plus standard intensive care with standard intensive care alone in term infants with perinatal asphyxial encephalopathy.

The primary endpoint was the combined incidence of mortality and severe neurodevelopmental disability in survivors at 18 months. The posted counts were 74 of 163 in the cooled arm and 86 of 162 in the non-cooled arm. The unadjusted risk difference was 0.077, with an interval from -0.032 to 0.185 and p = 0.166. The interval includes no difference.

The registry lists secondary outcomes and adverse-event summaries but no reported analyses. Details of the original sample-size justification, statistical plan, missing-data handling, and analysis populations are not reported in the registry record.