Impact of Deep Versus Standard Muscle Relaxation on Intra-operative Safety: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Impact of Deep Versus Standard Muscle Relaxation on Intra-operative Safety (NCT04124757), a randomized na study. The primary outcome is Classic Score>1.

2. Clinical Question

The registry describes uncertainty about whether improved surgical working conditions with deep blockade translate into fewer intra-operative and postoperative complications. The trial was intended to assess safety outcomes prospectively across multiple clinics and a variety of surgical procedures. The posted primary comparison concerns the incidence of events requiring intervention or treatment, rather than surgical working conditions alone.

The clinical question is about the difference between two blockade strategies within the trial’s laparoscopic surgery setting. It does not ask whether either strategy is better for every patient or every type of surgery. The registry record does not report detailed eligibility criteria, the number or identity of participating centers, or the distribution of surgical procedures. Those details limit how specifically the enrolled population can be characterized.

3. Trial Design

The registry identifies this as a randomized, triple-masked, parallel-group study sponsored by Leiden University Medical Center. The official title describes a multicenter strategy study of deep versus standard muscle relaxation during laparoscopic surgery. The recorded phase is not applicable. The study status is completed. The registry reports enrollment of 731 participants; the primary outcome results list 361 participants in the standard neuromuscular blockade group and 362 in the deep neuromuscular block group.

The comparator was standard neuromuscular blockade, described as a regular rocuronium induction dose with 10 mg boluses if conditions were insufficient. The deep-blockade strategy used a high-dose rocuronium induction followed by continuous administration, aiming for 1–2 twitches on post-tetanic count. The registry lists the deep-blockade intervention as an “other” intervention. It does not explain who was masked or how masking was maintained.

The primary outcome was assessed on the day of surgery. The registry describes the attending surgeon and anesthesiologist scoring the event at the end of each procedure. The Classic score is a six-point classification ranging from no complications (0) to fatal complications (5). The description also says the study used the original classic scoring and an adapted version of an updated classic scoring system that included anesthesia-related events. The posted primary result is titled “Classic Score>1.”

Secondary outcomes listed include the Leiden Surgical Rating Scale (L-SRS), 30-day postoperative complications, quality of recovery, and quality of life. Results are posted for the L-SRS and 30-day postoperative complications. Results for quality of recovery and quality of life are not reported in the registry record. The registry does not report the original sample-size justification, the planned analysis populations, or a detailed statistical analysis plan.

4. Participant Flow and Accounting

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

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 Classic Score>1, measured over Day of surgery.

The primary endpoint is the incidence of symptomatic intra-operative adverse events requiring intervention or treatment, classified as Classic ClassIntra grade >1 during laparoscopic surgery. The registry says the attending surgeon and anesthesiologist scored events at the end of each procedure. It describes the Classic score as a six-point scale, from no complications (0) to fatal complications (5). An adapted version of an updated classic scoring system was also used, with the update including anesthesia-related events.

This kind of endpoint is used to capture clinically consequential events during the operation, rather than every possible change in surgical conditions. Requiring intervention or treatment defines the events of interest for the posted primary outcome. The result is reported as the number of participants with an event in each group, allowing the comparison to focus on the proportion affected rather than the total number of procedures alone.

The wording of the endpoint and the posted result title are not identical in detail: the description refers to symptomatic events requiring intervention or treatment and a grade threshold, while the result title is “Classic Score>1.” The registry does not report further information about how the adapted score was applied in the primary analysis, how disagreements between assessors were handled, or whether adjudication was performed. Therefore, the posted counts should be interpreted according to the registry’s endpoint description without assuming additional scoring or adjudication procedures.

The endpoint addresses intra-operative safety on the day of surgery. It does not by itself summarize postoperative recovery, quality of life, or all aspects of surgical working conditions.

7. Results Posted in the Registry

• Deep Neuromuscular Block: 14.9% (54/362) versus 18.3% (66/361) on control; risk difference -3.4 percentage points (95% CI -8.8 to 2.1), risk ratio 0.82 (0.59–1.13); 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.

L-SRS (Leiden Surgical Rating Scale)

• 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:
  • Deep Neuromuscular Block: mean 4.90 versus 4.60 on control; difference 0.30 (95% CI 0.24 to 0.36), standardized effect d = 0.73; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Deep Neuromuscular Block than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

30 Day Post-operative Complications

• 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:
  • Deep Neuromuscular Block: 38.4% (139/362) versus 39.3% (142/361) on control; risk difference -0.9 percentage points (95% CI -8.0 to 6.2), risk ratio 0.98 (0.81–1.17); unadjusted two-proportion z-test p = 0.796.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deep Neuromuscular Block and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results add context about surgical conditions and recovery after surgery, but they address outcomes distinct from the primary intra-operative safety question. The L-SRS result concerns a rating on the day of surgery, while the postoperative-complication result concerns participants with complications over 30 postoperative days. The registry also lists quality of recovery and quality of life, but results for those outcomes are not reported in the registry record.

Across the two secondary outcomes with posted results, the numerical pattern is not the same: the L-SRS comparison has a positive mean difference with an unadjusted p-value <0.001, while the postoperative-complication comparison has a risk difference close to zero and an unadjusted p-value of 0.796. These results should not be combined into a single claim about overall benefit or safety. Each outcome captures a different aspect of the perioperative experience, and a change in a surgical rating does not automatically imply a change in complications.

In general, secondary outcomes are useful for describing other dimensions of a trial, but they often carry less confirmatory weight than a primary endpoint. Testing multiple outcomes creates more opportunities for chance findings. The registry does not report whether these secondary outcomes were ranked in a prespecified testing hierarchy or whether p-values were adjusted for multiple comparisons. The posted p-values are unadjusted, so the L-SRS finding should be interpreted with that limitation in mind rather than treated as definitive evidence based on its p-value alone.

The registry’s list includes four secondary outcomes, while results are posted for two. It is not reported in the registry record why the remaining outcomes lack posted results. Missing result postings should not be interpreted as evidence that an outcome was not measured, nor as evidence of a particular result. A complete interpretation would require the outcome definitions, analysis populations, missing-data information, and prespecified analysis plan, several of which are not reported in the registry record.

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

• L-SRS (Leiden Surgical Rating Scale)
• 30 Day Post-operative Complications
• Quality of Recovery (QoR)
• Quality of Life (QoL)

9. Statistical Interpretation

10. Statistical Methods Explained

Randomization assigns participants to study groups by chance. In general, this helps reduce systematic differences in measured and unmeasured characteristics between groups, although it does not guarantee that every characteristic will be balanced. The registry identifies this study as randomized and parallel-group: participants were assigned to one of two strategies, and the groups were compared. It does not report the randomization sequence method, allocation concealment procedures, or stratification factors.

What does the risk difference describe?

For an outcome recorded as participants with an event, the risk difference compares the event proportions in the two groups by subtracting the comparator-group proportion from the intervention-group proportion. A negative estimate for deep versus standard blockade means the observed event proportion was lower in the deep group. The primary estimate is -0.034. That direction describes the observed comparison; it does not establish that the true difference is negative. Its confidence interval extends from -0.088 to 0.021, including zero and values on either side.

The registry also posts relative measures for the primary comparison: a risk ratio of 0.816 with an interval from 0.587 to 1.134, and an odds ratio of 0.784 with an interval from 0.529 to 1.161. These are different ways of expressing a group contrast. A risk ratio compares the event proportions as a ratio; an odds ratio compares the event odds. Neither measure removes uncertainty, and both posted intervals include the no-difference value of 1. The primary risk difference is the clearest absolute contrast for understanding how far apart the observed group risks are.

How should a confidence interval be understood?

In general, a confidence interval is a range of values compatible with the observed data under the method used to calculate it. It expresses uncertainty about an estimate, rather than a range containing a known true effect with certainty. For a difference, zero is the value corresponding to no difference. When an interval includes zero, the data are compatible with no difference as well as with effects in either direction. An interval’s width also matters: wider intervals indicate less precision about the size of the effect. The registry does not report all details of the methods used to calculate the posted intervals.

What does the p-value add?

In general, a p-value measures how unusual data at least as different as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of a result. The primary unadjusted p-value is 0.224. This is consistent with the primary confidence interval including zero. The L-SRS unadjusted p-value is <0.001, while the postoperative-complication p-value is 0.796. These are unadjusted results; the registry does not report a multiplicity procedure. A p-value should therefore be considered alongside the estimate, interval, outcome definition, and the number of outcomes examined.

Why can outcome type matter?

Binary outcomes record whether each participant did or did not experience an event. Here, the primary endpoint and postoperative complications are reported as participant counts. Continuous outcomes, such as L-SRS, are summarized by group means and standard deviations. In general, the mean describes the average score, while the standard deviation describes variation among individual scores. Different outcome types require different statistical summaries and can have different precision even in the same participants.

General statistical methods also distinguish a prespecified primary endpoint from secondary outcomes. The primary endpoint is typically the central outcome for the main study question. Secondary endpoints may add context, but testing many outcomes increases the chance of observing a small p-value by chance if no adjustment is made. The registry lists several secondary outcomes and reports no analysis entries. It does not report whether a hierarchy, multiplicity adjustment, covariate adjustment, or sensitivity analysis was planned or used. Accordingly, the posted unadjusted secondary comparisons should not be treated as if they were adjusted confirmatory tests.

Confidence intervals and p-values depend on the statistical model and assumptions used. For example, general methods for counts may assume independent participant outcomes, while other analyses may account for clustering, repeated measurements, or covariates. The registry record does not report whether such approaches were used for the posted comparisons. The simple recalculations are unadjusted comparisons from posted summary statistics, so they do not replace a prespecified sponsor analysis. The discrepancy indicator is false, meaning no conflict between those calculations and the sponsor’s own analysis is flagged in the record.

11. Confidence Intervals and Precision

The primary risk difference is -0.034, with a 95% confidence interval from -0.088 to 0.021. This interval is important because it spans zero: the data are compatible with no difference and with a difference in either direction. The point estimate alone would leave out that uncertainty. The relative measures give a similar caution: the risk-ratio interval is 0.587 to 1.134, and the odds-ratio interval is 0.529 to 1.161. Both include 1, the no-contrast value for those measures.

In general, a confidence interval describes the precision of an estimate under the method used to construct it. Narrower intervals provide more precise estimates; wider intervals leave greater uncertainty about the size of the contrast. The primary interval leaves uncertainty about both direction and magnitude. It does not establish that the groups have equivalent outcomes, because equivalence requires a defined margin and an appropriate analysis; such a margin is not reported in the registry record.

The L-SRS mean difference is 0.3, with an interval from 0.240 to 0.360. This interval is relatively concentrated around its estimate, but precision about a score difference is not the same as evidence about the primary safety outcome. The registry does not report a threshold for a meaningful L-SRS difference. For 30-day postoperative complications, the risk difference is -0.009, with an interval from -0.080 to 0.062. This interval includes zero and a range of contrasts in either direction, so the result is not precise enough to conclude that the groups have the same complication experience.

Precision is affected by the amount of information available and the variability of an outcome, among other factors. The registry reports the group counts and estimates, but does not report the original precision target or the trial’s own sample-size rationale. Confidence intervals should be read as uncertainty about these specific posted contrasts, not as guarantees about outcomes in other settings.

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 give participants per arm for the binary outcomes, rather than a combined total across both groups. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses a stated fraction of the observed effect as the effect to detect. The registry does not report the trial’s own original design assumptions or sample-size justification, so these calculations should not be mistaken for the enrollment target used to plan the trial.

The 80% power column describes a planning scenario in which a study of the stated size would have an 80% chance of detecting the specified effect under the assumptions used, if that effect were real. The 90% power column uses a higher target chance of detecting that effect, and therefore generally requires more participants. For example, the primary-outcome illustration for 100% of the observed effect lists 1,918 participants per arm for 80% power and 2,567 participants per arm for 90% power. For 75% of the observed effect, the corresponding figures are 3,479 and 4,657 participants per arm. Smaller effects are harder to detect and need more participants for the same power target.

These figures are planning illustrations based on the observed effect, not observed power. They do not describe the probability that the trial’s result is true or the probability that a future trial will reproduce it. They also depend on the listed assumptions and on the estimated effect used as their starting point. Because observed effects can be uncertain, especially when the primary estimate has a confidence interval spanning zero, the illustrations are best read as examples of how sample-size requirements change with the assumed effect size.

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 = 0.183; treatment proportion p₁ = 0.149; average p̄ = 0.166.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5262 = 1.0313.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5257 = 0.4424.
4. n = (1.0313 + 0.4424)² / (-0.0337)² = 1,917.6, rounded up to 1,918 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 <- 0.182825484764543                          # control proportion
p1 <- 0.149171270718232                          # 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(4124757)
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 = 1,918 (80% power), 2,567 (90% power)
 75% of observed effect: n per arm = 3,479 (80% power), 4,657 (90% power)
 50% of observed effect: n per arm = 7,982 (80% power), 10,685 (90% power)
power.prop.test: 1917.6 
Simulated power at n = 1,918 per arm: 0.801 (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 several outcomes, comparisons, or analyses are examined. In general, the more tests performed, the greater the chance that at least one result appears statistically notable by chance alone. This is why prespecified primary and secondary outcome hierarchies, or statistical adjustment procedures, can matter when interpreting multiple results. The registry lists the primary endpoint and several secondary outcomes, but it does not report a multiplicity plan, a testing hierarchy, or an adjustment method.

The posted p-values are unadjusted. The L-SRS result has an unadjusted p-value <0.001, and the postoperative-complication result has an unadjusted p-value of 0.796. Those values should be read as endpoint-specific unadjusted comparisons rather than as results protected against the possibility of multiple testing. The registry does not report how many comparisons were planned beyond the listed outcomes, or whether other analyses were conducted.

The registry also does not report the analysis populations, including whether the primary comparison followed an intention-to-treat approach, whether participants were analyzed according to their assigned group, or whether exclusions occurred. It does not report participant-level missingness, outcome-specific missing data, or the method used to handle missing observations. The arm counts posted for individual outcomes are available, but the record does not explain how those counts relate to all enrolled participants or whether any participants lacked outcome data.

Other analysis details are also not reported in the registry record: covariate adjustment, center effects, protocol deviations, sensitivity analyses, and handling of departures from the assigned blockade strategy. The registry lists no reported analysis entries. This absence does not establish that no such analyses were performed; it means their details are not available in the registry record. Without these details, the posted group comparisons can be described, but their relationship to any prespecified full analysis plan cannot be evaluated.

In general, missing outcome or analysis information can affect confidence in how representative a posted estimate is of all randomized participants. That concern does not prove bias occurred. It identifies information needed to assess the risk of bias more fully. The registry record does not provide enough detail to determine the extent or likely direction of any missing-data or analysis-population effects.

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: unplanned readmission (6.6%).

The serious adverse event figures list 24 participants at risk and 24 affected in the standard neuromuscular blockade group, and 23 at risk and 23 affected in the deep neuromuscular block group. Deaths are listed as 0 in both groups. The most frequent serious adverse event term listed is unplanned readmission, reported as 6.6%. The registry does not attribute that term’s percentage to a particular group in the posted summary.

The other adverse event counts are 65 participants affected among 361 at risk in the standard group and 51 affected among 362 at risk in the deep group. These figures should be read as counts in the registry’s adverse-event listing, not as a complete account of every possible harm. The record does not provide detailed definitions of serious and other adverse events, event-level descriptions, or information on severity, timing, relatedness, or statistical comparisons.

Adverse-event counts are descriptive. A numerical difference between groups does not, by itself, establish that the assigned blockade strategy caused the difference. The registry also does not report methods for collecting or adjudicating adverse events. The counts therefore provide a limited view of the safety information posted in the record and should be considered alongside the primary endpoint and the trial’s other reported outcomes.

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

The primary result describes the observed difference in participants with symptomatic intra-operative adverse events requiring intervention or treatment. The point estimate favors fewer recorded events in the deep-blockade group, but the confidence interval includes zero and extends in both directions. The result therefore does not precisely establish a difference between groups for the primary endpoint. It also does not establish that the groups are equivalent; the registry does not report an equivalence margin or an analysis designed to demonstrate equivalence.

The L-SRS comparison shows a posted difference in mean surgical rating scores, with a confidence interval that does not include zero. This finding concerns a different outcome from the primary endpoint, and the registry does not provide a threshold for judging the clinical importance of the score difference. The posted postoperative-complication comparison does not precisely establish a difference, as its interval includes zero and values in both directions. These outcomes should not be collapsed into one overall conclusion.

In general, a trial result applies most directly to the population, procedures, outcome definitions, and study conditions represented in that trial. The registry describes a multicenter study during laparoscopic surgery, but detailed eligibility criteria, center information, and procedure mix are not reported. The results cannot automatically be extended to other surgical settings or patient groups based on the registry record alone.

The findings also do not establish why the groups may differ on an outcome. Randomization supports comparison of assigned strategies, but the registry does not report adherence, crossover, analysis-population details, or adjusted analyses. The posted results describe group outcomes; they do not settle all causal or mechanistic questions. The registry record also does not report results for quality of recovery or quality of life, despite listing those as secondary outcomes.

These results are statistical descriptions, not medical advice. They should be understood with their uncertainty, endpoint-specific meaning, and the limitations of the registry information in mind.

17. Why This Trial Matters Statistically

This study raises a practical statistical question: whether a strategy that changes neuromuscular blockade and is intended to improve working conditions also corresponds to a difference in intra-operative adverse events requiring intervention or treatment. The registry distinguishes the primary safety outcome from surgical working conditions and postoperative complications. That distinction matters because outcomes that seem clinically related are not interchangeable statistical endpoints.

The primary estimate is accompanied by a confidence interval that spans zero, so the point estimate alone would give an incomplete account of the evidence. The interval makes visible the uncertainty in the direction and size of the primary contrast. The posted L-SRS result, in contrast, is more clearly separated from zero statistically, but it measures a rating rather than the primary safety outcome. Reading the endpoints together without treating them as equivalent avoids overstating what any one result says.

The trial also illustrates why planning assumptions matter. Planning illustrations based on an observed effect can require substantially different numbers of participants depending on the assumed effect size and power target. Such illustrations can help explain the relationship between effect size, precision, and sample size, but they are not a substitute for the trial’s original design justification. That justification is not reported in the registry record.

Finally, the distinction between primary and secondary results is important. Unadjusted findings across multiple outcomes need cautious interpretation, particularly when the registry does not report a prespecified testing hierarchy or multiplicity adjustment. The study provides useful posted comparisons, while the missing analysis and outcome details limit how fully their planned statistical context can be assessed.

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 does not report the original sample-size justification or the trial’s planned design assumptions. The sample-size illustrations are based on observed effects and specified planning assumptions, not on documentation of how enrollment was chosen. The record also does not provide a detailed statistical analysis plan, analysis populations, or a list of prespecified covariates and sensitivity analyses.

Information on missing outcome data and participant flow is limited. The registry reports enrollment of 731 and primary outcome group counts of 361 and 362, but does not explain how the outcome counts relate to all enrolled participants. Reasons for any unavailable data, exclusions, or deviations from assigned treatment are not reported. The record does not describe adherence to the intended blockade strategies or crossover between strategies.

The registry identifies randomization and triple masking but does not specify the randomization procedure, allocation concealment, which individuals were masked, or how masking was maintained. It does not report the number or identities of participating centers, detailed eligibility criteria, or the mix of laparoscopic procedures. These omissions limit assessment of study conduct and the applicability of results to particular settings.

The primary endpoint description refers to symptomatic events requiring intervention or treatment and to an adapted scoring system, while the posted result is titled “Classic Score>1.” Additional detail on the exact operational definition, scoring disagreements, and adjudication is not reported. The registry lists four secondary outcomes, but results for quality of recovery and quality of life are not reported. It also provides no multiplicity plan, and the posted secondary p-values are unadjusted.

These limitations identify information that would be useful for a fuller statistical assessment. They do not establish that the trial was conducted improperly or that the posted estimates are biased.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Impact of Deep Versus Standard Muscle Relaxation on Intra-operative Safety — NCT04124757.
• Registry record last updated 2025-06-11; status last verified 2025-05.
• Results first posted 2025-06-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04124757 is a completed, randomized, triple-masked, parallel-group study sponsored by Leiden University Medical Center. Its official title describes a multicenter strategy study comparing deep and standard muscle relaxation during laparoscopic surgery. Enrollment was 731.

The primary outcome was the number of participants with symptomatic intra-operative adverse events requiring intervention or treatment, assessed on the day of surgery. The posted primary risk difference for deep versus standard neuromuscular blockade is -0.034, with a 95% confidence interval from -0.088 to 0.021 and an unadjusted p-value of 0.224. The interval includes zero, leaving uncertainty about the direction and size of the difference.

Results are also posted for L-SRS and 30-day postoperative complications. Quality of recovery and quality of life are listed as secondary outcomes, but their results are not reported in the registry record. The registry does not report the original sample-size justification, detailed analysis plan, multiplicity handling, or analysis populations.