Normobaric Hyperoxia for Intracerebral Hemorrhage: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Normobaric Hyperoxia for Intracerebral Hemorrhage (NCT04144868), a randomized phase 2 study. The primary outcome is Percentage of Patients With mRS 0-3.

2. Clinical Question

The clinical rationale in the registry focuses on perihematoma tissue and the possibility that improving oxygen availability could affect injury around the hematoma. The trial was described as a proof-of-concept evaluation of NBO in intracerebral hemorrhage. Its primary endpoint captures disability status at follow-up rather than an imaging change alone. Hematoma and perihematomal edema measurements at 3 days were also posted as secondary outcomes. Those imaging measurements offer a different view of the results from the 90-day disability endpoint, but they do not replace it.

3. Trial Design

The registry describes a randomized, double-masked, parallel-group phase 2 trial sponsored by Capital Medical University. It was a single-center study and is marked completed. Enrollment was 96. The registry lists a start date of 2020-01-15 and a primary completion date of 2021-12-31.

Participants were assigned to the NBO group or the control group. The intervention differed in oxygen-delivery method and schedule: NBO used intermittent high-flow mask oxygen with nasal-catheter oxygen during the intervening periods, while control care used nasal-catheter oxygen continuously. Both regimens were described as beginning at admission and continuing for 7 days. The registry identifies the devices as oxygen storage face masks and nasal catheters.

Double masking means that the study record identifies the trial as masked at two levels, but it does not specify in the posted details who was masked or how masking was maintained. The allocation method beyond the designation “randomized,” the sequence-generation procedure, and any concealment procedures are not reported in the registry record. The original protocol’s statistical plan and the assumptions used to choose the trial’s enrollment target are also not reported in the registry record.

The primary outcome was the count of participants with an mRS score of 0–3 at 90 days. The posted groups each include 48.0 participants for this endpoint. The registry also lists secondary outcomes covering NIHSS scores, Glasgow Coma Scale, Barthel Index, mRS distribution, hematoma volume, and perihematomal edema. Three imaging outcomes have group summaries and unadjusted comparisons posted at 3 days; detailed outcome analyses are not posted for the other listed secondary measures.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients With mRS 0-3, measured over 90 days.

The primary endpoint is the number of participants with an mRS score from 0 to 3 at 90 days. The modified Rankin Scale is an ordinal measure of global disability. Its range is described in the registry as 0 (no symptoms) to 6 (death). The primary endpoint groups scores 0 through 3 together and counts how many participants fall within that range.

Using a defined score range turns the ordinal scale into a binary outcome for this comparison: a participant is either counted in the 0–3 category or is not. This makes the result interpretable as a group-level difference in the fraction meeting the selected threshold. It also means the endpoint does not display the full distribution of scores. Participants with different scores inside the 0–3 range are counted together, as are all scores outside that range. The secondary outcome list includes mRS distribution, which can describe the broader spread of scores, but its detailed results are not posted in the registry record.

A 90-day disability measure addresses status at follow-up, whereas the imaging outcomes at 3 days describe earlier structural measurements. These outcomes answer related but distinct questions. The mRS endpoint is therefore useful for describing the trial’s primary clinical comparison, while the imaging measures provide additional information about the biological and radiological context. The registry’s primary outcome description does not state a separate analysis population or explain why this particular threshold was selected.

7. Results Posted in the Registry

• NBO Group: 81.2% (39/48) versus 56.2% (27/48) on control; risk difference 25.0 percentage points (95% CI 7.1 to 42.9), risk ratio 1.44 (1.09–1.92); unadjusted two-proportion z-test p = 0.008.

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.

Hematoma Volume

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • NBO Group: mean 14.89 versus 16.80 on control; difference -1.91 (95% CI -4.53 to 0.71), standardized effect d = -0.30; z-test p = 0.153.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NBO Group and the control. The interval gives the range of effects that remain compatible with the data.

Absolute Perihematomal Edema Volume

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • NBO Group: mean 30.51 versus 33.51 on control; difference -3.00 (95% CI -7.51 to 1.51), standardized effect d = -0.27; z-test p = 0.192.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NBO Group and the control. The interval gives the range of effects that remain compatible with the data.

Relative Perihematomal Edema Volume

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • NBO Group: mean 1.99 versus 1.94 on control; difference 0.05 (95% CI -0.16 to 0.26), standardized effect d = 0.10; z-test p = 0.647.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NBO Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several kinds of information: neurological scores, level of consciousness, daily functioning, mRS distribution, and imaging measures of hematoma and perihematomal edema. This breadth can help readers see whether the primary endpoint sits alongside related clinical or structural observations. The secondary outcome list alone, however, does not establish that each measure was analyzed or that each was planned as confirmatory.

Among the secondary results with group summaries and comparisons posted, the three imaging outcomes at 3 days show a mixed pattern rather than a consistent direction across every measure. Their unadjusted confidence intervals include zero. These findings do not provide clear statistical corroboration of the primary comparison, but neither do they establish that the imaging groups were equivalent. The measures assess different quantities, and differences in measurement scale and timing limit direct comparison with the 90-day mRS outcome.

The registry lists 17 secondary outcomes posted, while the detailed group summaries and unadjusted comparisons available in the record cover only a subset. Formal reported analyses for the three imaging comparisons are not listed. Detailed results for the other secondary measures are not reported in the registry record. This means the secondary material cannot be treated as a complete account of all planned or collected outcomes.

Multiplicity is a concern whenever many outcomes or comparisons are examined. With more opportunities to observe a seemingly notable result, the chance of at least one result appearing unusual by chance can increase. Because the registry does not report a multiplicity strategy, unadjusted secondary results carry less inferential weight than a prespecified primary endpoint. Their appropriate role is to describe patterns and generate questions, rather than to independently confirm the primary result.

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

• NIHSS Scores
• NIHSS Scores
• NIHSS Scores
• Glasgow Coma Scale
• Glasgow Coma Scale
• Glasgow Coma Scale
• Barthel Index
• mRS Distribution

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant is classified according to whether the 90-day mRS score falls from 0 to 3. For a binary endpoint, a group proportion describes the fraction of participants with the event of interest. A risk difference compares the two proportions by subtracting one group’s proportion from the other’s. Here, the reported risk difference is 0.25, with the NBO group as the comparison group and control as the reference. It is an absolute difference on the proportion scale, not a relative ratio.

A confidence interval gives a range of values that are reasonably compatible with the observed data under the statistical method used. It expresses uncertainty in the estimated group difference; it is not a range containing a fixed proportion of individual participant outcomes. The primary interval is 0.071 to 0.429. Its relation to zero is relevant because zero would represent no difference on the risk-difference scale. The registry also reports an unadjusted p-value of 0.008. A p-value summarizes how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of the observed difference.

The primary comparison is unadjusted in the posted statistics. An unadjusted comparison uses the group-level outcome counts without accounting for other covariates. Randomization is intended to support a fair comparison between assigned groups, but the registry does not report the specific primary-analysis model, any covariate adjustment, or the analysis population. The exact trial analysis method and any prespecified handling of missing observations are not reported in the registry record.

For continuous outcomes, the posted summaries give the group mean and standard deviation. A mean is the arithmetic average, while a standard deviation describes how spread out individual measurements are around that average. The comparison is a mean difference, expressed as the NBO group mean minus the control group mean. A negative mean difference therefore corresponds to a lower group mean in NBO; a positive value corresponds to a higher group mean. The interval for a mean difference describes uncertainty in that estimated contrast. If the interval includes zero, the data are compatible with no mean difference as well as with differences in either direction under the calculation used.

The imaging comparisons are based on group summaries at 3 days. The registry gives the number analyzed for these summaries as 46.0 in each group. These numbers are not the same as the primary outcome group counts, and the record does not explain the difference between the posted outcome counts. It does not state whether this reflects missing measurements, exclusions, or another reason. The method used to address any such difference is not reported in the registry record.

Standard deviation and standard error describe different sources of variation. A standard deviation characterizes variability among participant measurements; a standard error characterizes uncertainty in an estimated statistic, such as a group mean. General statistical interpretation should not treat them as interchangeable. For the continuous outcomes, the record reports standard deviations for the groups and also includes values used in the comparison calculations, but it does not report formal secondary analyses.

For binary outcomes, relative measures such as a risk ratio or odds ratio compare groups on a multiplicative scale rather than an absolute-difference scale. They can present the same underlying comparison in a different way, and their numerical size is not directly interchangeable with a risk difference. The registry includes relative estimates for the primary endpoint, but the risk difference is used for the main interpretation above. Any relative estimate should be read with its own interval and scale in mind.

Over-dispersion is a general concern when observations vary more than a chosen model expects. In that situation, standard errors can be too small if the model assumes less variability than the data contain, making intervals too narrow and tests too optimistic. It is not possible to assess whether over-dispersion was considered for the trial’s analyses because the statistical model and diagnostic procedures are not reported in the registry record. This general issue is especially relevant when a model’s assumptions determine how uncertainty is estimated; it should not be taken as evidence that over-dispersion occurred in this trial.

The record’s unadjusted comparisons provide a readable summary of the posted group data, but they do not supply the full context needed to reproduce a trial analysis. The protocol analysis plan, the prespecified estimand, procedures for missing data, any sensitivity analyses, and the multiplicity strategy are not reported in the registry record. The interpretation should therefore distinguish the reported group summaries and unadjusted comparisons from any broader claims about the trial’s planned inferential framework.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated group difference. The primary risk-difference estimate is 0.25, and its 95% confidence interval runs from 0.071 to 0.429. The interval is entirely above zero, so the posted estimate is compatible with a positive difference on the risk-difference scale under the method used. The interval’s width also shows that the exact size of the difference remains uncertain; the point estimate should not be treated as a precise prediction of what would be observed in another study.

A confidence interval describes uncertainty in the estimate, not the range of participant-level outcomes. It does not mean there is a 95% probability that the true effect lies inside this particular interval. Under repeated use of the same method and assumptions, confidence intervals have a long-run coverage interpretation. This general explanation does not establish which exact inferential method was used in the registry comparison.

The primary interval is more informative about precision than the p-value alone. A p-value gives evidence relative to a null model, while the interval displays a range of effect sizes compatible with the data. Both are unadjusted in the posted comparison. The record does not report whether adjustment for other variables or a different analysis population would alter the estimate or its precision.

The secondary imaging comparisons have intervals that include zero, indicating that their posted estimates are less decisive about the direction of a difference. This does not prove that the groups are identical. It indicates that the available data and reported calculations do not pin down those contrasts with the same clarity as a narrow interval excluding zero would. The sample sizes for those measurements are 46.0 per group, and the registry does not state why these differ from the primary outcome counts.

Precision is also affected by the amount of information available, the variability of measurements, and the analysis method. The trial’s original assumptions for planning enrollment and its procedures for handling missing data are not reported in the registry record. Consequently, the posted intervals are best read as the uncertainty attached to the reported comparisons, rather than as a complete account of the study’s design or all sources of uncertainty.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a specified fraction of the observed effect as the effect to detect: 100%, 75%, or 50% of the observed effect.

In general, a power target describes the probability that a planned study would detect an effect of the specified size under the assumed model and significance threshold, if that effect were present. The 80% column gives the per-arm planning count for the 80% target; the 90% column gives the per-arm count for the 90% target. A higher target generally requires more participants under the same assumptions. Likewise, smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm.

These numbers are planning illustrations calculated from the observed effect, not the trial’s own design calculation. The original trial’s sample-size justification and design assumptions are not reported in the registry record. The planning figures are not observed power: they do not measure the probability that the completed trial’s result is true or the probability that a treatment effect exists. They show how estimated enrollment requirements change under the stated assumptions and effect scenarios.

For continuous outcomes, the planning illustrations relate to the mean-difference summaries; for the primary binary outcome, they relate to the risk-difference summary. These calculations rely on the normal approximation stated in the record and should be understood as illustrations rather than a reconstruction of the trial protocol. They also do not account for design features or analysis choices that are not described in the registry record.

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 = 0.562; treatment proportion p₁ = 0.812; average p̄ = 0.688.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6555 = 1.2848.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6312 = 0.5312.
4. n = (1.2848 + 0.5312)² / (0.2500)² = 52.8, rounded up to 53 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 <- 0.5625                          # control proportion
p1 <- 0.8125                          # 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(4144868)
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 = 53 (80% power), 71 (90% power)
 75% of observed effect: n per arm = 100 (80% power), 133 (90% power)
 50% of observed effect: n per arm = 235 (80% power), 314 (90% power)
power.prop.test: 52.8 
Simulated power at n = 53 per arm: 0.810 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, subgroups, or comparisons. Each additional test creates another opportunity for a result to appear notable by chance. Statistical strategies can control the overall chance of false-positive conclusions, or researchers may identify a single primary comparison and treat the rest as exploratory. The registry lists multiple secondary outcomes, but a multiplicity adjustment or hierarchy for testing them is not reported in the registry record.

The primary endpoint is identified, and its comparison is posted with an unadjusted p-value. The record does not state whether that value was adjusted for any other analyses or whether a prespecified testing sequence was used. The secondary outcome record includes no reported formal analyses for the detailed imaging comparisons. Without the analysis plan, it is not possible to determine which secondary outcomes were intended as confirmatory or how their results were meant to be interpreted alongside the primary endpoint.

Missing-data handling is also not reported in the registry record. The primary endpoint summaries list 48.0 participants in each group, whereas the three posted imaging outcomes list 46.0 per group. The registry does not explain the difference, report missingness by reason, or describe any imputation or sensitivity procedure. The difference in the reported group counts should not be assigned a cause without those details.

The primary outcome description does not identify an analysis population, such as all randomized participants or only participants with observed outcomes. The record also does not report whether participants were analyzed according to assigned group, how protocol deviations were handled, or whether additional populations were used. Those elements affect how an estimate should be understood and whether it corresponds directly to the randomized assignment.

In the absence of these details, the posted result can be described as the registry’s unadjusted comparison of the reported outcome counts. It cannot establish the trial’s full prespecified inferential plan, the extent of missing outcome data, or the robustness of the conclusion to alternative assumptions. These omissions limit interpretation without changing the numerical results that are posted.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record lists 48 participants at risk in each group. Serious adverse events affected 0 participants in the NBO group and 0 in the control group. Other adverse events affected 12 participants in each group. Deaths are listed as 0 in both groups, and no serious adverse-event terms are listed.

These counts describe what the registry record reports; they do not show the severity, timing, duration, or specific nature of the other adverse events. The record does not provide a detailed account of how events were collected or adjudicated, or whether event reporting was complete for all participants. A zero count in the serious-event entries means no serious events are recorded in those fields, not that the trial establishes the absence of risk. The adverse-event figures should be interpreted as descriptive counts from this record rather than as a comprehensive safety assessment.

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

The primary result describes a difference between randomized groups in the number of participants recorded with an mRS score of 0–3 at 90 days. The estimate is 0.25 on the risk-difference scale, and the 95% confidence interval is 0.071 to 0.429. This is evidence about the observed comparison in this trial, with uncertainty around the size of the difference. It is not a guarantee that the same estimate would occur in another study or setting.

The result does not, by itself, establish the mechanism behind the group difference. The endpoint is a disability category at 90 days, while the imaging outcomes are measurements at 3 days. Their relationship is not established by the posted summaries. Nor does the primary result show the full distribution of mRS scores, because the endpoint groups scores 0–3 together and counts participants within that range.

The study is described as a phase 2 proof-of-concept trial. That context matters when interpreting the scope of the evidence. The registry record does not report the original sample-size justification, detailed analysis plan, missing-data methods, or multiplicity strategy. These omissions prevent a full appraisal of the planned inferential approach from the registry record alone. The posted secondary imaging comparisons do not provide a consistent, clearly resolved pattern that independently confirms the primary result.

The safety entries list no serious adverse events and no deaths in either group, along with 12 other adverse events in each group. Those recorded counts should not be interpreted as proof of no risk, because the record does not give details of ascertainment or event characteristics. The overall meaning is therefore limited to the outcomes and counts recorded, the uncertainty around the primary comparison, and the information available about trial conduct and analysis.

These data do not dictate a clinical decision. They describe one randomized comparison in a particular trial and should be considered together with the full study report and other relevant evidence. The registry does not provide enough detail to resolve all questions about analysis populations, outcome completeness, or how secondary findings were planned to be used.

17. Why This Trial Matters Statistically

This trial is statistically informative because it makes a randomized comparison of an intervention strategy with a defined control regimen and reports a primary outcome at a specified follow-up time. The primary endpoint is clinically interpretable as the count of participants in an mRS range, while its binary form permits a direct absolute comparison between groups. The reported risk difference and confidence interval communicate both the direction of the observed contrast and uncertainty about its magnitude.

The trial also illustrates why statistical interpretation should not rest on a p-value alone. The interval provides a range of compatible values on the outcome scale, while the p-value summarizes evidence relative to a null model. The secondary outcomes add context, but their mixed pattern and unadjusted status do not turn them into independent confirmation. Reading outcomes by their role and timing helps avoid treating every endpoint as equally decisive.

The record also demonstrates the value of complete reporting. Information about the analysis population, missing-data procedures, multiplicity, and original sample-size assumptions would help readers understand how the reported result relates to the trial plan. The difference between primary and imaging outcome counts is visible in the record, but its explanation is not reported. Clear reporting of such details supports more transparent interpretation and replication.

Finally, the planning illustrations show how participant requirements depend on assumptions about target effect size, power, and allocation. They are not evidence that the completed study was adequately or inadequately powered, and they are not observed power. Separating planning calculations from trial results is essential when using registry data to assess precision and future study design.

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 describes a single-center phase 2 trial, which limits how much can be inferred about the consistency of results across other settings. Enrollment was 96. The record does not report details of recruitment, participant characteristics, eligibility criteria, or the degree to which the enrolled group represents a broader population. These limits make it difficult to judge the reach of the findings from the registry alone.

Several important design and analysis details are not reported in the registry record. These include the randomization procedure, who was masked, the original sample-size justification, the statistical analysis plan, the primary analysis population, and the methods used to handle missing data. The primary outcome counts differ from the group counts posted for the imaging measurements, but the reason is not reported. This prevents a clear assessment of how complete each outcome’s analysis set was.

The posted secondary material is incomplete in relation to the broad outcome list. Detailed results for some listed secondary measures are not reported in the registry record, and formal analyses are not listed for the imaging comparisons. A multiplicity strategy is also not reported, so secondary findings should be treated cautiously. The trial’s posted unadjusted comparisons do not reveal whether additional prespecified or sensitivity analyses were performed.

Safety reporting is limited to counts of serious and other adverse events and deaths. Event descriptions, timing, severity, and ascertainment methods are not reported in the registry record. The record therefore supports a description of the entries, but not a comprehensive assessment of safety or event capture.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Normobaric Hyperoxia for Intracerebral Hemorrhage — NCT04144868.
• Registry record last updated 2025-04-30; status last verified 2025-04.
• Results first posted 2025-04-30.
• 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 record describes a completed, randomized, double-masked, parallel-group phase 2 trial of normobaric hyperoxia for intracerebral hemorrhage. Enrollment was 96, with 48.0 participants in each group for the primary outcome. The primary endpoint was the number of participants with an mRS score of 0–3 at 90 days.

The posted comparison reports 39.0 participants in the NBO group and 27.0 in the control group meeting that endpoint, with a risk difference of 0.25 and a 95% confidence interval from 0.071 to 0.429. Three imaging outcomes at 3 days have group summaries and unadjusted comparisons; their intervals include zero. Safety entries list 0 serious adverse events and 12 other adverse events in each group, with 0 deaths in both groups.

The registry does not report the original sample-size justification, detailed analysis plan, missing-data procedures, multiplicity strategy, or primary analysis population. These omissions limit interpretation beyond the posted outcome summaries and comparisons.