Cerebral Autoregulation Monitoring During Cardiac Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cerebral Autoregulation Monitoring During Cardiac Surgery (NCT00981474), a randomized na study. The primary outcome is Composite Neurological Outcome of Clinical Stroke or New Ischemic Brain Lesion on Diffusion Weighted MRI or Neurocognitive Dysfunction 4 to 6 Weeks After Surgery..

2. Clinical Question

The trial addresses a monitoring-and-management strategy during surgery. Its central contrast is not simply whether a monitoring signal can be measured, but whether using autoregulation information to set blood pressure targets is associated with a different postoperative neurological outcome than empiric institutional targets. The registry describes neurological complications as an important concern in cardiac surgery and presents the intervention as a strategy intended to reduce brain injury related to inadequate brain blood flow.

The primary result is a composite: an event could be clinical stroke, a new ischemic lesion detected by postoperative diffusion weighted magnetic resonance imaging, or cognitive decline from baseline to 4-6 weeks after surgery. Those components differ in how they are identified and in their clinical manifestation. The composite therefore captures several forms of neurological injury rather than stroke alone. Interpretation should remain tied to that defined outcome and to the population who completed the required neurological and MRI testing.

3. Trial Design

The registry describes a randomized, double-masked, parallel-group trial with enrollment of 460. The listed phase is NA. The study is marked completed. The registry dates are 2009-09-01 for study start and 2020-02-04 for primary completion. Northwestern University is listed as sponsor.

Participants were assigned to usual care or autoregulation-guided management. In the control group, blood pressure targets during cardiopulmonary bypass followed institutional standards of empiric management. In the intervention group, blood pressure management was based on cerebral autoregulation data. The interventions are labeled “Control group” and “blood pressure maintenance based on cerebral blood flow autoregulation measurement” in the record; the arm descriptions clarify the management contrast.

The primary outcome was assessed up to 6 weeks post-operative. It combined clinical stroke, new ischemic lesions on postoperative diffusion weighted MRI, and cognitive decline from baseline to 4-6 weeks after surgery. The primary population is specified as subjects who completed neurological testing and MRI testing. That definition matters: the reported primary analysis counts do not describe every enrolled participant, and the record does not report a complete accounting of why people did or did not contribute to that analysis.

The registry lists postoperative delirium, prolonged use of multiple inotropic drugs, prolonged mechanical lung ventilation, insertion of an intra-aortic balloon pump, postoperative atrial fibrillation, sepsis, acute kidney injury, and new renal replacement therapy among secondary outcomes. It records 11 outcome measures and 11 analyses, with 10 secondary outcomes posted. The record does not report the trial’s original sample-size justification, detailed allocation procedures, masking procedures, or statistical analysis plan. Those details should not be inferred from the randomized and double-masked design labels.

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: After obtaining written informed consent, 468 were randomized to the two groups. 237 in the autoregulation group were randomized after consent and 5 subjects withdrew consent. 231 in the usual care group were randomized after consent and 3 subjects withdrew consent.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Subjects who completed neurological testing and MRI testing

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 Composite Neurological Outcome of Clinical Stroke or New Ischemic Brain Lesion on Diffusion Weighted MRI or Neurocognitive Dysfunction 4 to 6 Weeks After Surgery., measured over Up to 6 weeks post-operative.

The primary endpoint is a composite neurological outcome, measured as the number of participants with clinical stroke, a new ischemic lesion on postoperative diffusion weighted MRI, or cognitive decline from baseline to 4-6 weeks after surgery. The timeframe is up to 6 weeks post-operative. The stated analysis population comprises subjects who completed neurological testing and MRI testing.

A composite can represent more than one clinically relevant manifestation of a broader problem. Here, it brings together a clinical event, an imaging finding, and a neurocognitive change. This may capture neurological injury that would not be represented by clinical stroke alone. However, the components are not interchangeable: a finding on MRI and a change in cognitive testing differ in their detection and meaning from a clinical stroke. The combined result should therefore be interpreted as the frequency of the defined composite, not as a result for each component separately.

The registry’s rationale describes brain injury related to inadequate brain blood flow as the concern motivating the monitoring strategy. A composite endpoint can be useful when an intervention is expected to affect several related outcomes, but it can also make the overall finding depend on how often each component occurs. Component-specific primary results are not reported in the registry record. The posted endpoint result answers the composite question for the stated analysis population; it does not establish that every component changed in the same way.

7. Results Posted in the Registry

• Autoregulation Group: 75.3% (70/93) versus 78.2% (79/101) on control; risk difference -2.9 percentage points (95% CI -14.9 to 9.0), risk ratio 0.96 (0.82–1.12); unadjusted two-proportion z-test p = 0.627.

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.

Postoperative Delirium

• 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:
  • Autoregulation Group: 8.2% (19/232) versus 14.9% (34/228) on control; risk difference -6.7 percentage points (95% CI -12.5 to -0.9), risk ratio 0.55 (0.32–0.93); unadjusted two-proportion z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Autoregulation Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Multiple Inotropic Drugs>24 Hours After Surgery

• 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:
  • Autoregulation Group: 2.6% (6/232) versus 5.7% (13/228) on control; risk difference -3.1 percentage points (95% CI -6.8 to 0.5), risk ratio 0.45 (0.18–1.17); unadjusted two-proportion z-test p = 0.093.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Autoregulation Group and the control. The interval gives the range of effects that remain compatible with the data.

Mechanical Lung Ventilation>24 Hours After Surgery

• 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:
  • Intervention: 5.6% (13/232) versus 9.6% (22/228) on control; risk difference -4.0 percentage points (95% CI -8.9 to 0.8), risk ratio 0.58 (0.30–1.12); unadjusted two-proportion z-test p = 0.102.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The registry records 10 secondary outcome measures, covering postoperative delirium, inotropic drug use, prolonged ventilation, intra-aortic balloon pump insertion, atrial fibrillation, sepsis, acute kidney injury, and new renal replacement therapy. The detailed secondary results include different event patterns across outcomes rather than a uniform pattern of estimates. Some recalculated comparisons favor the autoregulation group, while others are less conclusive. This broad pattern does not provide a consistent secondary basis for overturning the uncertain primary result.

Secondary outcomes can help describe other postoperative events and may suggest questions for further study. They do not change the definition or result of the primary neurological composite. Nor do secondary estimates establish effects on the components of that composite unless those components are separately analyzed and reported. Component-specific primary comparisons are not reported in the registry record.

Unadjusted secondary results carry less weight because repeated testing across multiple outcomes increases the opportunity for chance findings. The registry record does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or a procedure for designating confirmatory results. Consequently, a nominally notable secondary comparison should be treated cautiously, especially when the primary outcome remains uncertain. The secondary outcomes are best interpreted as descriptive or hypothesis-generating evidence in this record, not as independent proof of a treatment effect.

The outcome definitions and analysis populations also differ across the registry entries. For example, the primary population is specified by completion of neurological testing and MRI testing, while the secondary outcomes have their own recorded group counts and timeframes. Comparisons across outcomes therefore do not necessarily refer to the same assessed population or observation period. The overall secondary pattern is informative context, but it does not provide a single pooled conclusion about the intervention.

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

• Postoperative Delirium
• Multiple Inotropic Drugs>24 Hours After Surgery
• Mechanical Lung Ventilation>24 Hours After Surgery
• Insertion of Intra-aortic Balloon Pump
• Postoperative Atrial Fibrillation
• Sepsis
• Acute Kidney Injury Within 7 Days After Surgery.
• New Renal Replacement Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is between randomized parallel groups: usual care and blood pressure management based on cerebral autoregulation data. Randomization is intended to make the groups comparable, on average, with respect to both measured and unmeasured baseline characteristics. It does not guarantee identical groups, and the registry record does not report the randomization sequence, allocation concealment, or any stratification factors. Those details are not reported in the registry record.

What does the risk difference describe?

A risk difference expresses the difference between the proportions experiencing an event in the two groups. It is an absolute-scale measure: a negative estimate for the autoregulation group indicates a lower observed event proportion in that group relative to usual care. The recalculated primary risk difference is -0.029. Its confidence interval extends from -0.148 to 0.089, so the data remain compatible with a range of absolute differences, including directions on either side of no difference. This calculation is unadjusted and is based on the posted summary counts.

How does a risk ratio differ?

A risk ratio compares the event risks as a relative measure rather than subtracting them. The registry-reported primary risk ratio is .96, with a 95% confidence interval from .82 to 1.121. A ratio near its no-association reference describes similar risks; values on either side represent relative decreases or increases. The interval includes values on either side of that reference, which indicates uncertainty about the direction and size of the relative association. Risk differences and risk ratios answer related but distinct questions, and their numerical estimates are not directly interchangeable.

What is the role of the p-value?

The recalculated unadjusted primary p-value is 0.627, and the registry reports p = .752 for its risk-ratio analysis. A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the probability that the result will replicate. A larger p-value does not establish equivalence or prove that groups are identical. The size and precision of the estimated effect, along with the design and analysis population, matter for interpretation.

Why distinguish reported and recalculated analyses?

The recalculated estimates are simple unadjusted calculations from posted summary statistics. The sponsor’s analysis is the analysis recorded by the trial, while the recalculation provides a transparent comparison using the reported counts. They can differ because the measures and analysis procedures differ; the primary record reports a risk ratio, while the recalculation gives a risk difference. The registry record does not report enough detail to reconstruct the sponsor’s full statistical procedure beyond the listed Chi-squared method and its reported risk-ratio analysis.

Why does the endpoint definition matter?

The outcome counts participants with any component of a composite: clinical stroke, new ischemic brain lesion on postoperative diffusion weighted MRI, or cognitive decline from baseline to 4-6 weeks after surgery. An analysis of the composite treats any qualifying component as an event, but the overall estimate cannot reveal component-specific effects. The stated analysis population also requires completion of neurological testing and MRI testing. The analysis therefore pertains to that population as recorded, not automatically to every randomized participant.

The registry labels the trial double-masked, but it does not describe which participants, clinicians, assessors, or analysts were masked, nor how masking was maintained. The registry record does not report whether the primary statistical model included covariate adjustment, how missing values were handled, or whether there were interim analyses. These methodological details should not be assumed. The uncertainty interval is a statistical description under its analysis assumptions; it does not address possible bias from incomplete outcome ascertainment or other design limitations.

For binary outcomes, uncertainty is especially relevant when event counts are limited. Confidence intervals reflect sampling variability under the analysis method, while unadjusted comparisons do not account for potential differences in baseline characteristics or multiplicity. An interval can be broad even when a point estimate favors one group. In general, a confidence interval presents a range of effect estimates reasonably compatible with the observed data and model, rather than a range guaranteed to contain the true effect.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.029, with a confidence interval from -0.148 to 0.089. This interval is wide enough to include estimates on both sides of no difference. The point estimate alone therefore gives an incomplete account: its direction favors fewer composite events in the autoregulation group, but the interval indicates that the data do not pin down the size or direction precisely.

The registry’s risk-ratio estimate is .96, and its 95% confidence interval runs from .82 to 1.121. Because the interval includes values on either side of the no-association reference, it does not precisely distinguish a relative reduction from a relative increase. The recalculated risk-difference interval and the registry risk-ratio interval use different scales, but both communicate uncertainty in the primary comparison.

In general, a confidence interval describes the range of values compatible with the data under a statistical model and repeated-sampling procedure. It is not a guarantee that the true effect lies within the particular interval, and it does not assign a probability to a particular treatment effect. Width reflects statistical precision: narrower intervals indicate greater precision, while wider intervals leave more plausible values unresolved. Precision is not the same as clinical importance.

The primary analysis uses the outcome population described as subjects who completed neurological testing and MRI testing. The registry record does not explain how this population arose from enrollment or report the impact of missing primary outcomes. The uncertainty intervals quantify sampling variation as represented by the analysis; they do not automatically account for selection or bias that could arise if outcome completion were related to group assignment or neurological status.

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 sample-size illustrations translate observed effects into hypothetical planning requirements. For the listed binary outcomes, the figures are participants per arm, not total participants. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect, if that effect and the other assumptions were correct. The 90% column applies the same idea at a higher chance of detection, which generally requires more participants. Rows for planning at 75% or 50% of the observed effect consider smaller effects than the full observed effect; smaller effects need more participants to distinguish them from chance variation at the stated significance level.

For the primary endpoint, planning for 100% of the observed effect gives 3,221 participants per arm for 80% power and 4,311 participants per arm for 90% power. Planning for 75% gives 5,663 participants per arm for 80% power and 7,580 participants per arm for 90% power. Planning for 50% gives 12,597 participants per arm for 80% power and 16,863 participants per arm for 90% power.

These are planning illustrations based on the observed effect, not a reconstruction of the trial’s original design or evidence about the probability that the completed trial detected an effect. This is not observed power. The observed effect can be imprecise, so the illustrations should be read as conditional planning scenarios rather than definitive sample-size recommendations.

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 = 0.782; treatment proportion p₁ = 0.753; average p̄ = 0.767.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5975 = 1.1710.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5971 = 0.5025.
4. n = (1.1710 + 0.5025)² / (-0.0295)² = 3,220.4, rounded up to 3,221 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 <- 0.782178217821782                          # control proportion
p1 <- 0.752688172043011                          # 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(981474)
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 = 3,221 (80% power), 4,311 (90% power)
 75% of observed effect: n per arm = 5,663 (80% power), 7,580 (90% power)
 50% of observed effect: n per arm = 12,597 (80% power), 16,863 (90% power)
power.prop.test: 3220.4 
Simulated power at n = 3,221 per arm: 0.799 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Chi-squared analysis of the risk ratio: .96, with a 95% confidence interval from .82 to 1.121 and p = .752. The recalculated summary-statistic analysis gives an unadjusted risk difference of -0.029, with a confidence interval from -0.148 to 0.089 and p = 0.627.

These estimates are expressed on different scales. The sponsor’s risk ratio compares relative risks, while the recalculated risk difference compares absolute risks. Their point estimates should not be compared numerically as though they represented the same quantity. Both analyses indicate that the primary comparison is uncertain: neither reported interval clearly separates the groups from the no-effect reference for its measure.

The registry record marks no discrepancy between the reported analysis and the recalculation. Even so, the sponsor’s analysis is the trial’s recorded analysis; the recalculation is a simple unadjusted check using the posted group counts. The registry does not report sufficient detail to reproduce every aspect of the sponsor’s procedure. Differences in measure and method can affect estimates and p-values without implying that either result is a transcription error.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary composite and multiple secondary outcomes, but does not report a multiplicity plan. It is not reported in the registry record whether the investigators adjusted secondary p-values, prespecified a testing hierarchy, or controlled a family-wise error rate. Without such information, secondary p-values should be understood as unadjusted unless the registry explicitly states otherwise. When many outcomes are examined, some apparently notable results may occur by chance, so a secondary finding generally warrants less confidence than a prespecified primary comparison.

The primary analysis population is described as subjects who completed neurological testing and MRI testing. The registry reports primary outcome counts of 79 among 101 in usual care and 70 among 93 in the autoregulation group, while the study enrollment is 460. Secondary entries use their own denominators, including 228 for usual care and 232 for the autoregulation group in the detailed postoperative outcomes. These figures should not be combined or treated as if they represent one common analysis population. The registry does not report a participant flow accounting that explains these differences.

Missing-data handling is not reported in the registry record. It is not reported whether incomplete assessments were excluded, imputed, classified as having no event, or addressed through sensitivity analyses. The reasons for missing neurological testing or MRI results are also not reported. This limits assessment of whether the analyzed primary population could differ systematically from the randomized groups.

The record does not report whether the primary analysis followed an intention-to-treat approach, whether any per-protocol or other population was used, or how deviations from assigned management were handled. Nor does it report interim analyses, stopping rules, covariate adjustment, or a detailed analysis plan. The randomized design supports a causal comparison in principle, but interpretation depends on execution and analysis choices that cannot be evaluated from the registry summary alone.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: new ischemic lesions in brian (60.8%), acute kidney injury (26.7%), delayed neurocognitive recovery (21.3%), clinical stroke (5.6%), sepsis (3.1%).

The registry’s serious adverse event entries list 228 participants at risk in the usual-care group, with 133 affected, and 232 at risk in the autoregulation group, with 121 affected. For other adverse events, it lists 34 affected among 228 at risk in usual care and 19 among 232 at risk in the autoregulation group. The deaths entries are 12 and 5, respectively. These are the recorded counts; the registry summary does not establish that differences between groups are caused by the management strategy.

The record also lists serious-event terms with percentages, including New Ischemic Lesions in Brian at 60.8%, Acute Kidney Injury at 26.7%, Delayed Neurocognitive Recovery at 21.3%, Clinical Stroke at 5.6%, Sepsis at 3.1%, and Multisystem Organ Failure after Surgery at 2.6%. The registry does not clarify in this summary whether terms can overlap within participants or how each percentage was calculated. They should not be added or treated as mutually exclusive categories.

These safety entries are descriptive. A group count alone does not account for event severity, timing, exposure, or baseline risk, and the registry summary does not provide a comparative safety analysis with uncertainty intervals. The entries therefore provide context about recorded events, not a definitive causal assessment.

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

The primary data show an observed composite event frequency that was lower in the autoregulation group than in usual care, with the recalculated risk difference favoring the intervention. However, the confidence interval is broad and includes estimates in both directions, and the registry’s reported risk-ratio interval also includes values consistent with no clear difference. The posted results are therefore uncertain about the size and direction of the primary effect.

That uncertainty is not proof that the two management approaches are equivalent. A study can fail to distinguish a difference from chance variation while still leaving effects of practical importance compatible with its confidence interval. Conversely, a point estimate in a favorable direction does not demonstrate that the intervention caused a reduction. The data should be read through the estimates and their precision, not through direction alone.

The result concerns a composite neurological endpoint among subjects who completed neurological testing and MRI testing. It does not establish a separate effect on clinical stroke, MRI lesions, or cognitive decline, because component-specific estimates are not reported in the registry record. It also does not automatically generalize to people outside the recorded surgical setting or to management strategies different from the specified comparison.

Secondary outcomes offer additional postoperative context but involve multiple comparisons and do not resolve the primary uncertainty. The registry does not report a multiplicity plan, missing-data methods, or enough detail to evaluate the full statistical analysis. Those limitations make cautious interpretation appropriate. The registry record documents a randomized trial and its posted results; it does not alone establish a definitive clinical conclusion about the monitoring strategy.

No medical decision should be inferred from these statistical results alone. The evidence summarized by the registry is one part of an assessment that would also require clinical context, study conduct details, and consideration of other relevant evidence. Such information is not reported in the registry record.

18. Why This Trial Matters Statistically

This trial is statistically instructive because the primary point estimate and its uncertainty tell different parts of the story. The point estimate favors autoregulation-guided management, but the interval spans effects in both directions. Reading only the estimate would overstate certainty; reading only the p-value would discard information about the range of effects compatible with the data.

It also illustrates why the outcome population must be read alongside enrollment. The primary composite is reported for participants who completed neurological testing and MRI testing, with denominators that differ from the enrollment figure and from the denominators used for detailed secondary outcomes. Without a participant flow description or missing-data analysis, the effect of incomplete outcome ascertainment cannot be assessed from the registry summary.

The endpoint’s composite structure is another important statistical feature. Combining clinical stroke, imaging findings, and cognitive change broadens the outcome but can conceal variation among components. A result for the combined endpoint does not imply that each component has the same frequency pattern or treatment response. Component-level reporting would be needed to answer those separate questions.

Finally, the registry’s secondary outcomes and safety counts demonstrate the distinction between descriptive data and confirmatory inference. Multiple unadjusted outcomes can produce interesting signals, but without a stated multiplicity strategy they should not be treated as independent confirmation. The record therefore provides a useful example of interpreting randomized evidence with attention to effect scale, uncertainty, analysis population, endpoint construction, and the boundaries of registry reporting.

19. Limitations

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

Several trial-specific details needed for a full appraisal are not reported in the registry record. The primary endpoint population is restricted to subjects who completed neurological testing and MRI testing, but the record does not provide participant flow or reasons for unavailable assessments. The relationship between the primary analysis denominators and the randomized enrollment therefore cannot be fully evaluated. Missing-data methods and sensitivity analyses are not reported.

The primary outcome combines clinical stroke, new ischemic MRI lesions, and cognitive decline. The registry gives the composite result but does not report primary component-specific estimates. This limits understanding of which elements contributed to the observed result and whether the composite components followed similar patterns. The registry also does not report the detailed cognitive assessment method or thresholds used to define decline.

The analysis plan is not reported in sufficient detail to assess covariate adjustment, intention-to-treat handling, interim analyses, stopping rules, or prespecified multiplicity control. The registry identifies the study as double-masked but does not describe masking roles or procedures. The original sample-size justification is not reported; the planning illustrations are based on the observed effect and are not the trial’s original design calculation.

Some secondary outcomes are reported with different labels and timeframes, and the detailed secondary denominators differ from those for the primary analysis. The summary does not describe whether adverse event categories overlap, nor does it give a full comparative safety analysis. These limitations do not invalidate the posted estimates, but they constrain what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cerebral Autoregulation Monitoring During Cardiac Surgery — NCT00981474.
• Registry record last updated 2026-06-05; status last verified 2026-05.
• Results first posted 2021-03-02.
• 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.

23. Record Summary

The registry record describes a completed randomized, double-masked, parallel-group trial with enrollment of 460, sponsored by Northwestern University. It compares blood pressure management based on cerebral autoregulation data with usual care based on institutional standards during cardiopulmonary bypass.

The primary outcome is a composite of clinical stroke, new ischemic lesions on postoperative diffusion weighted MRI, or cognitive decline from baseline to 4-6 weeks after surgery, assessed in subjects who completed neurological testing and MRI testing. The recalculated unadjusted risk difference is -0.029, with a confidence interval from -0.148 to 0.089 and p = 0.627. The registry reports a risk ratio of .96, with a 95% confidence interval from .82 to 1.121 and p = .752.

The posted primary estimates are uncertain. Secondary outcome and safety entries add descriptive context, while important details about missing data, multiplicity, and the original statistical plan are not reported in the registry record.