Electroencephalography Guidance of Anesthesia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Electroencephalography Guidance of Anesthesia (NCT02241655), a randomized na study. The primary outcome is Number of Participants With Delirium.

2. Clinical Question

The study's broader stated aim included postoperative delirium and its downstream effects, as well as patient-reported health-related quality of life. The registry also lists postoperative falls and health-related quality of life as secondary outcomes. These broader aims provide context, but the primary statistical comparison is specifically about whether participants were counted as having postoperative delirium during the stated assessment window. It does not by itself answer every question about later function, quality of life, or other outcomes.

3. Trial Design

ENGAGES was a randomized, parallel-group trial with triple masking, according to the registry record. It was sponsored by Washington University School of Medicine and has completed. The registry lists the phase as not applicable. Enrollment was 1400; the primary-outcome description separately reports that 1232 patients were randomized, with 614 assigned to EEG-guided anesthesia and 618 to standard care. These figures describe different registry fields and should not be treated as interchangeable counts without additional information about the trial record.

The intervention was a pragmatic protocol that used electroencephalography to guide anesthetic administration. Practitioners were to modify anesthesia in an attempt to limit burst suppression or persistent suppression. The control group received the standard anesthetic protocol. The parallel design compares outcomes between these separately assigned groups rather than comparing each participant with themselves under both protocols.

The primary outcome was the number of participants with postoperative delirium, assessed for up to 5 days after surgery. Assessment used the Confusion Assessment Method for verbal patients or the Confusion Assessment Method for the Intensive Care Unit for nonverbal or intubated patients. Medical records were also reviewed for evidence of delirium based on doctors' and nurses' assessments. A participant was considered to have delirium if any modality identified it at any point from postoperative day one through five.

The registry lists 18 outcome measures and 6 analyses, but the original statistical analysis plan, including the full prespecified analysis hierarchy, is not reported in the registry record. The trial's own sample-size justification, anticipated effect, and design assumptions are also not reported in the registry record. The dates listed are a start in 2015-01 and primary completion on 2018-05-17.

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: 1400 participants were consented to the study168 were not randomized to a study treatment arm (2 died, 49 were ineligible after enrollment, 49 surgery was cancelled, 31 research team missed the surgery, 37 withdrew). A total of 1232 patients were randomized to a study arm.

Overall Study

Analysis population for the primary outcome, as defined in the registry: A total of 1232 patients were randomized (614 EEG guided protocol and 618 control arm). In the EEG guided group 10 patients could not be assessed for delirium (6 comatose, 2 withdrew, 2 early hospital discharge). In the control arm 9 patients could not be assessed for delirium (1 died, 5 comatose, 1 withdrew, 2 early hospital discharge).

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 Number of Participants With Delirium, measured over 5 days.

The primary endpoint counts participants who experienced postoperative delirium during the specified assessment period. It is a binary participant-level outcome: each assessed participant contributes either a delirium event or no recorded delirium event under the registry definition. The endpoint is not a count of separate delirium episodes, duration, or severity. A participant identified by any of the assessment routes at any time from postoperative day one through five was considered to have delirium.

Delirium is relevant to the study's stated aim of evaluating postoperative outcomes in older surgical patients. A defined assessment window and use of structured assessment approaches make it possible to compare the proportion of participants meeting the outcome definition across randomized groups. Including medical-record review alongside assessments tailored to verbal and nonverbal patients helps capture cases in different clinical circumstances, as described in the record.

Interpretation depends on both the case definition and the observation process. The record states that assessment occurred at baseline and once daily postoperatively for up to 5 days, but it does not provide further detail on assessor training, adjudication, or how conflicting modalities were handled. It reports that some randomized patients could not be assessed for delirium. The reported outcome groups therefore have smaller denominators than the randomized groups. The registry record does not fully report the reasons for all patients who could not be assessed.

This endpoint addresses occurrence within the short postoperative window, not all downstream effects named in the study aim. It should be interpreted alongside the available secondary outcomes and the limitations of follow-up and outcome reporting.

7. Results Posted in the Registry

• EEG Guided Protocol: 26.0% (157/604) versus 23.0% (140/609) on control; risk difference 3.0 percentage points (95% CI -1.8 to 7.8), risk ratio 1.13 (0.93–1.38); unadjusted two-proportion z-test p = 0.224.

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.

The Number of Participants With Postoperative Falls

• 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:
  • EEG Guided Protocol: 28.9% (136/471) versus 28.0% (135/482) on control; risk difference 0.9 percentage points (95% CI -4.9 to 6.6), risk ratio 1.03 (0.84–1.26); unadjusted two-proportion z-test p = 0.767.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EEG Guided Protocol and the control. The interval gives the range of effects that remain compatible with the data.

The secondary-outcome record is much less complete than the primary-outcome record. Postoperative falls and health-related quality of life are listed as secondary outcomes, but quantitative results are posted for falls only. Results for health-related quality of life are not reported in the registry record. The available secondary information therefore does not permit a broad assessment across all listed secondary outcomes.

Across the primary delirium outcome and the available falls outcome, the posted estimates do not provide a clear, precise pattern of separation between the groups. This overall reading is consistent with the primary comparison's uncertainty, but the endpoints concern different outcomes and follow-up windows. They should not be combined as though they measured one common effect, nor should the secondary outcomes be used to replace or override the primary endpoint.

Secondary results generally carry less weight than a prespecified primary result because there may be multiple outcomes and analyses, increasing the chance that an apparently notable finding arises by chance. The registry record lists 18 outcome measures and 6 analyses, but does not report the complete testing hierarchy or a multiplicity adjustment plan. The available falls analysis is identified as chi-squared with an odds ratio, and its reported p-value is unadjusted. Without a clear account of which secondary tests were planned and how multiplicity was handled, an isolated secondary result is less conclusive.

Secondary outcomes can still be useful for describing the range of outcomes examined and for motivating further research. Their value depends on complete reporting, prespecification, adequate precision, and appropriate interpretation in the context of all analyses. The registry record does not provide enough information to establish those features for every listed secondary outcome.

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

• The Number of Participants With Postoperative Falls
• Health Related Quality of Life

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference represent?

The primary comparison reports a risk difference for EEG-guided anesthesia relative to control. A risk is the proportion of participants in a group who experienced the binary outcome. The risk difference subtracts the control risk from the intervention-group risk, so a positive estimate indicates a higher observed risk in the intervention group, while a negative estimate indicates a lower observed risk. The posted estimate is 0.030. This is an absolute contrast, not a ratio; it describes the difference in outcome proportions on the probability scale.

The two group risks used in the comparison are 0.260 and 0.230, based on 157 of 604 participants and 140 of 609 participants, respectively. Keeping the denominators in view is important because the randomized groups were 614 and 618. The primary-outcome description reports that some participants could not be assessed, and the record does not fully explain all differences between randomized and analyzed counts.

How should the confidence interval be read?

A confidence interval expresses uncertainty in an estimate under the statistical method used. The primary risk-difference interval runs from -0.018 to 0.078. Its lower end is below zero and its upper end is above zero, so the interval includes both a lower and a higher risk in the EEG-guided group relative to control. It also includes no difference. The interval is not a list of all possible true effects, nor does it assign a probability to any one value. Rather, it shows the range of values reasonably compatible with the observed data and the method's assumptions.

A wide interval indicates that the estimate is not highly precise. The interval's breadth should be considered together with the point estimate, the outcome counts, and the trial's reporting. A confidence interval does not correct for missing outcome data, selective reporting, or departures from the assumed analysis model.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.224. A p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted label matters: the registry record does not report a multiplicity-adjusted primary p-value or give enough detail to establish the complete family of tests that may have been considered.

The p-value and confidence interval are related summaries of the same comparison, but the interval is more informative about the range and direction of effects compatible with the data. Neither one alone determines whether a difference is important. That judgment would also depend on a clinically meaningful threshold, which is not reported in the registry record.

Why distinguish randomized and outcome-analysis counts?

Randomization establishes the assigned groups at the start of the trial. The primary outcome counts use 604 and 609 participants rather than the randomized totals of 614 and 618. The record notes patients who could not be assessed, but the handling of every missing outcome and the exact analysis population are not fully described. An analysis restricted to people with an observed outcome can be affected if the probability of missingness is related to group assignment or outcome status. The direction and magnitude of any such effect cannot be inferred from these counts alone.

An intention-to-treat analysis generally seeks to retain participants in the groups to which they were randomized, regardless of treatment received, while a complete-case analysis uses participants with observed outcomes. The registry record does not establish which named analysis population was used for the posted primary comparison. These are general methodological distinctions, not claims about the trial's actual analysis.

What is the role of a binary-outcome comparison?

For an outcome recorded as whether a participant experienced delirium, the analysis compares event proportions between groups. The risk difference is one useful scale because it reports an absolute contrast. Relative measures, such as a risk ratio or odds ratio, express the contrast differently and can emphasize different aspects of the same data. They should not be treated as interchangeable with an absolute difference. A complete clinical interpretation would consider the outcome definition, baseline risk, follow-up window, missingness, and uncertainty, rather than relying on a single measure.

The registry includes a reported chi-squared analysis for postoperative falls, expressed as an odds ratio. That reported secondary analysis is distinct from the primary risk-difference comparison. A chi-squared test evaluates evidence of association between group and a categorical outcome under its assumptions. The odds ratio describes relative odds, not a risk difference or risk ratio. The record does not state further model details for that secondary analysis.

Why can over-dispersion matter?

Over-dispersion is a general concern when a statistical model assumes more consistency in outcomes than the data support. It is especially relevant for counts or clustered observations, where variability can exceed the model's assumed level. The primary outcome is recorded as participants with an event, rather than as a repeated event count, and the registry does not report a dispersion parameter or an over-dispersion adjustment. Therefore, over-dispersion should not be attributed to this trial's primary analysis. In general, when present, it can make standard errors too small and confidence intervals too narrow unless the model accounts for the extra variability.

Across all outcomes, statistical methods need to match the outcome scale and design. The registry record identifies randomization and parallel groups, but the full statistical analysis plan, including model specifications, handling of missing data, and any prespecified covariate adjustment, is not reported in the registry record. Statistical explanations of methods therefore clarify general interpretation without filling in those unreported choices.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.030, with a 95% confidence interval from -0.018 to 0.078. The interval includes zero and extends in both directions around it. This means the posted data are not precise enough to rule out either a lower or a higher delirium proportion in the EEG-guided group relative to control under the reported comparison. The interval also includes effects that may differ substantially in practical interpretation, but the registry record does not specify a threshold for clinical importance.

Precision concerns how tightly the data locate an estimated effect. It is distinct from whether an estimate is statistically significant or clinically important. The p-value of 0.224 is consistent with the interval including no difference, but the interval communicates more about the size and direction of effects compatible with the data. The point estimate should not be read in isolation: uncertainty around it is substantial enough that the direction of the underlying difference is not resolved by this comparison.

Observed outcome counts were 157 of 604 in the EEG-guided group and 140 of 609 in control. The randomized totals were 614 and 618. The primary outcome description notes 10 and 9 patients, respectively, could not be assessed. Missing outcome information can affect both the estimate and its precision, and the available record does not give enough detail to evaluate the missingness mechanism or all analysis choices.

Confidence intervals rely on assumptions about the analysis and data. They do not account automatically for possible outcome misclassification, departures from the planned analysis, or selective reporting. The registry record does not provide the full statistical analysis plan or a prespecified clinically important difference. Consequently, precision can be described statistically, but the practical importance of every value in the interval cannot be determined from the record alone.

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 illustration gives participants per arm for the binary outcomes, not total events. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a stated fraction of the observed effect. The original trial design's sample-size assumptions and justification are not reported in the registry record; these displayed planning assumptions are separate from that original design.

The 80% power column describes the approximate participants per arm needed, under those assumptions, for an 80% chance of detecting the selected effect if that effect were the true one. The 90% power column uses the same idea with a higher target chance of detection, and therefore generally requires more participants. The rows for planning for 75% or 50% of the observed effect ask about detecting smaller effects than the full observed estimate. Smaller effects are harder to distinguish from random variation, so more participants are required.

For the primary comparison, the illustrative values range from 3,214 participants per arm for planning for 100% of the observed effect at 80% power to 16,853 participants per arm for planning for 50% of the observed effect at 90% power. Each entry is a planning illustration, not a count of participants enrolled in ENGAGES. These figures are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval; the planning values instead show how sample-size needs depend on the effect one aims to detect and the chosen power target.

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 = 0.230; treatment proportion p₁ = 0.260; average p̄ = 0.245.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6082 = 1.1920.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6078 = 0.5115.
4. n = (1.1920 + 0.5115)² / (0.0300)² = 3,213.9, rounded up to 3,214 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 <- 0.229885057471264                          # control proportion
p1 <- 0.259933774834437                          # 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(2241655)
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 = 3,214 (80% power), 4,302 (90% power)
 75% of observed effect: n per arm = 5,655 (80% power), 7,570 (90% power)
 50% of observed effect: n per arm = 12,589 (80% power), 16,853 (90% power)
power.prop.test: 3213.9 
Simulated power at n = 3,214 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, groups, or analysis approaches. With many statistical tests, the chance of finding at least one apparently unusual result can increase even if there are no true effects. The registry lists 18 outcome measures and 6 analyses. It does not report a complete prespecified hierarchy identifying which outcomes were primary, how secondary comparisons were prioritized, or whether any correction for multiple testing was planned. A multiplicity strategy is therefore not reported in the registry record.

The primary result is accompanied by an unadjusted p-value. The registry does not report an adjustment for testing across outcomes or analyses. This does not by itself establish that an adjustment was required or omitted from the trial's full analysis; it means that the registry record does not document the approach. Secondary findings should consequently be viewed as exploratory or descriptive unless their prespecification and multiplicity handling are established elsewhere in the record.

Missing outcome data also affect interpretation. The registry reports that 10 participants assigned to EEG-guided anesthesia and 9 assigned to control could not be assessed for delirium. The reasons listed for the EEG-guided group include 6 comatose, 2 withdrew, and 2 early hospital discharge. For control, the record begins to list reasons but does not fully report them; it identifies 1 died and 5 comatose before the remaining description is incomplete. The registry record does not fully report how missing delirium status was handled analytically.

The randomized totals were 614 and 618, while the primary outcome analysis counts were 604 and 609. The record does not clearly state whether the posted analysis followed an intention-to-treat principle, used only participants with observed outcomes, or applied another approach. Nor does it report sensitivity analyses for missing outcomes. These omissions limit assessment of possible bias if missingness depended on group or underlying delirium status.

The record also does not provide a complete analysis plan, definitions of all analysis populations, or a detailed account of outcome adjudication. These are reporting limitations, not proof that the trial was conducted improperly. They restrict what can be concluded from the registry record about multiplicity, missing-data assumptions, and robustness.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: respiratory failures (4.4%), other gi event (2.9%), other body system event (2.3%), wound infection (2.1%), ileus/bowel obstruction (2.0%).

The registry reports serious adverse events in 124 of 614 participants in the EEG-guided group and 130 of 618 in control. Other adverse events are reported for 361 of 614 and 345 of 618, respectively. Deaths are listed as 4 and 20. These are descriptive group counts; the record does not provide a statistical comparison or an adjusted analysis of these safety figures. It also does not establish in the posted information whether each event was judged related to the intervention.

The leading serious-event terms listed include respiratory failures at 4.4%, other GI event at 2.9%, other body system event at 2.3%, wound infection at 2.1%, ileus/bowel obstruction at 2.0%, and cardiac arrest at 1.9%. These percentages describe the listed terms as recorded and should not be interpreted as comparative treatment effects without group-specific event detail and a defined analysis.

Adverse-event summaries can involve participants with more than one event, and the registry record does not explain whether categories overlap or how event severity and attribution were determined. Counts alone do not establish causation. They are best read as a description of events recorded in each group, alongside the limitations in reporting and without drawing a treatment conclusion from them.

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

The posted primary result estimates the difference in the proportion of participants recorded as having postoperative delirium during the assessment period. The estimate is 0.030 for EEG-guided anesthesia relative to control, with a 95% confidence interval from -0.018 to 0.078. This interval includes no difference and values on both sides of no difference. The result therefore leaves uncertainty about both the direction and magnitude of the group contrast.

The estimate does not prove that the protocols are identical. A failure to demonstrate a statistically clear difference is not the same as evidence of equivalence or noninferiority. Such conclusions require prespecified margins and suitable analyses, which are not reported in the registry record. Conversely, the positive point estimate alone does not establish that EEG guidance caused a higher delirium rate. The comparison is an estimate from the posted outcome data, with uncertainty and incomplete reporting that should remain visible in interpretation.

The result applies to the endpoint as defined: delirium identified by one of the stated assessment routes at any time from postoperative day one through five. It does not directly answer whether there were differences in delirium severity, duration, recurrence, later cognitive outcomes, or all downstream effects. Postoperative falls and health-related quality of life are listed as secondary outcomes, but health-related quality-of-life results are not reported in the registry record.

Randomization supports a comparison between assigned groups, but the posted outcome denominators are smaller than the randomized totals. Some participants could not be assessed for delirium, and the registry does not fully explain the handling of missing outcomes. The registry record also does not provide the full analysis plan or enough detail to evaluate every possible source of bias. Accordingly, the result should be understood as a statistical estimate for the reported analysis population and outcome definition, not as a complete account of every consequence of either anesthetic approach.

No medical decision follows from a p-value or interval alone. Practical interpretation would require evidence about meaningful effect thresholds, the complete trial methods, and the broader outcomes of interest. Those details are not all reported in the registry record. The statistical evidence presented supports careful description of the estimated contrast and its uncertainty rather than a categorical claim about benefit, harm, or equivalence.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about a complex intervention: how should outcomes be compared when the intervention is a pragmatic protocol implemented during surgery and the primary endpoint depends on repeated postoperative assessment? The registry's delirium definition combines structured instruments suited to different patient communication circumstances with medical-record review. That breadth can support case detection, while also making clear specification of assessment, adjudication, and missingness important for interpretation.

The randomized parallel-group design provides a framework for comparing assigned strategies. The primary outcome is a binary participant-level measure over a defined postoperative window, and the risk difference communicates the contrast on an absolute scale. Its confidence interval is essential: the point estimate alone would conceal that the data remain compatible with effects in either direction. Statistical interpretation is therefore about both the estimate and how much uncertainty surrounds it.

The record also illustrates why randomized enrollment, outcome-analysis denominators, and missing-outcome reporting should be distinguished. A difference between randomized and analyzed counts need not invalidate a comparison, but it does make the analysis population and missing-data approach relevant. Complete reporting would help readers judge how well the estimate reflects the randomized groups.

Finally, multiple outcomes and analyses make transparent prespecification important. The registry lists numerous outcome measures and analyses, yet the full hierarchy and multiplicity plan are not reported. This affects how strongly secondary findings can be interpreted and how the primary result fits into the full study. These issues are broadly relevant to clinical trials that examine several postoperative outcomes: clear outcome definitions, complete follow-up reporting, and transparent analysis plans make estimates easier to assess without overstating what the data establish.

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 are specific to the available registry record. The primary endpoint description reports that some randomized participants could not be assessed, and the outcome analysis uses smaller group counts than the randomized totals. Although reasons are listed for the EEG-guided group, the control-group reasons are not fully reported. The registry does not state clearly how missing outcome status was handled, whether any imputation or sensitivity analysis was used, or precisely which analysis population generated the posted comparison.

The delirium outcome combines assessment by different modalities and medical-record review. The record identifies the methods and the assessment window but does not report assessor training, blinding of outcome assessors, adjudication procedures, or resolution of discordant assessments. These details could matter for consistency of outcome classification. Triple masking is listed for the trial, but the registry record does not specify how masking applied to each role or whether it could be maintained during anesthetic care.

The full statistical analysis plan is not reported in the registry record. Details on covariate adjustment, prespecified contrasts, missing-data assumptions, multiplicity control, and analysis populations are therefore unavailable. The trial's original sample-size justification and design assumptions are also not reported. The planning illustrations based on the observed effect cannot substitute for those original design details.

Secondary reporting is incomplete: postoperative falls have a reported analysis, while health-related quality-of-life results are not reported in the registry record. Although the record lists 18 outcome measures and 6 analyses, it does not provide a complete account of the outcome hierarchy or all analysis decisions. The safety figures are descriptive and do not include a reported comparative analysis or complete information on event attribution. These limits concern the interpretability and completeness of the registry information; they should not be treated as evidence that unreported procedures were or were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Electroencephalography Guidance of Anesthesia — NCT02241655.
• Registry record last updated 2026-10-29; status last verified 2025-12.
• Results first posted 2019-06-18.
• 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

ENGAGES (NCT02241655) was a completed randomized, triple-masked, parallel-group trial sponsored by Washington University School of Medicine. Enrollment is listed as 1400. The primary outcome was the number of participants with delirium during assessment for up to 5 days after surgery. The posted primary comparison included 604 participants assigned to EEG-guided anesthesia and 609 assigned to control, with 157 and 140 delirium outcomes, respectively.

The estimated risk difference was 0.030, with a 95% confidence interval from -0.018 to 0.078 and an unadjusted p-value of 0.224. The interval includes no difference and effects in either direction. The record lists postoperative falls and health-related quality of life as secondary outcomes, but quantitative results for health-related quality of life are not reported in the registry record. Important details about the original sample-size plan, full statistical analysis plan, multiplicity handling, and missing-data analysis are not reported in the registry record.