Methohexital v Propofol as General Anesthetic in Patients on ACEIs or ARBs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Methohexital v Propofol as General Anesthetic in Patients on ACEIs or ARBs (NCT02624050), a randomized na study. The primary outcome is Number of Participants Who Had Hypotensive Events.

2. Clinical Question

The clinical question concerns hypotension occurring during a defined early period of anesthetic induction, rather than a broad measure of blood pressure over the entire surgical episode. The registry describes assignment to either anesthetic and identifies hypotensive events as the primary outcome. It also lists related outcomes, including refractory hypotension, episode duration, blood pressure, heart rate, and circulating hormone measurements. Those measures can characterize different aspects of hemodynamic response, but they do not replace the primary event-count question.

The registry record does not establish that the trial was designed to prove one drug safer or more effective in all settings. Its posted result pertains to the recorded study groups and outcome. Broader eligibility criteria, clinical definitions beyond the registry description, and details about how the findings might apply to other patients are not reported in the registry record.

3. Trial Design

The registry classifies the study as randomized, with a parallel-group model and no masking. Participants were assigned to receive either methohexital or propofol as general anesthetic induction. The listed doses were intravenous methohexital at 1.5mg per kg of patient body weight and intravenous propofol at 2.5mg per kg of patient body weight. The record describes a completed study, with enrollment of 51 participants. The posted primary outcome groups include 20 participants in the methohexital arm and 25 in the propofol arm.

Random allocation is intended, in general, to reduce systematic differences between treatment groups at the point of assignment. A parallel design means the groups receive separate assigned interventions rather than crossing over between them. With no masking, assignment was not concealed from participants or study personnel in the way it would be in a masked trial; the consequences of that design feature depend on how outcomes are assessed and managed. Further details of allocation implementation, concealment, and outcome assessment are not reported in the registry record.

The primary outcome was the number of participants with hypotensive events during the first 15 minutes of anesthetic induction. The registry also lists secondary outcomes covering refractory hypotension, duration of each episode, systolic and diastolic blood pressure, heart rate, and blood concentrations of norepinephrine, epinephrine, and angiotensin II. The record lists 11 outcome measures and 3 analyses. Whether all listed measures were collected at every stated time point, and how repeated measurements were modeled, is not reported in the registry record.

The trial's original sample-size justification, intended effect size, planned statistical procedures beyond the analyses posted, and any interim analyses are not reported in the registry record. The planning illustrations associated with the observed results are not evidence of the study's original design assumptions.

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

Reasons for not completing this period:

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 Who Had Hypotensive Events, measured over Hemodynamic measurements will be taken during the first 15 minutes of anesthetic induction.

The primary endpoint counts participants who experienced a hypotensive event during anesthetic induction. The registry specifies that hemodynamic measurements were taken during the first 15 minutes of induction, and describes the primary outcome as hypotensive events under either anesthetic. The outcome is therefore a participant-level event count: it records whether participants were counted as having an event, rather than the duration or severity of each episode.

This type of endpoint is useful for comparing how often an event was recorded in two groups. It gives a direct summary of event occurrence over the stated observation window, while avoiding the need to treat each measurement time or each episode as an independent participant. It does not, by itself, describe how low blood pressure fell, how long hypotension lasted, whether an episode was refractory, or the pattern of blood pressure over time. Those aspects are represented by distinct secondary outcomes in the registry.

Interpretation depends on the outcome definition and ascertainment. The registry provides the event-count description and observation period, but operational thresholds for hypotension, rules for multiple episodes in one participant, and procedures for resolving uncertain measurements are not reported in the registry record. The primary endpoint should therefore be read as the registry's recorded count of participants with hypotensive events, not as a complete description of every dimension of hemodynamic response.

7. Results Posted in the Registry

• Propofol: 84.0% (21/25) versus 40.0% (8/20) on control; risk difference 44.0 percentage points (95% CI 18.2 to 69.8), risk ratio 2.10 (1.20–3.69); unadjusted two-proportion z-test p = 0.002.

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.

Number of Participants With Refractory Hypotension

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Propofol: 20.0% (5/25) versus 10.0% (2/20) on control; risk difference 10.0 percentage points (95% CI -10.5 to 30.5), risk ratio 2.00 (0.43–9.24); unadjusted two-proportion z-test p = 0.358.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Propofol and the control. The interval gives the range of effects that remain compatible with the data.

Duration of Each Hypotension Episode

• 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:
  • Propofol: mean 4.80 versus 5.10 on control; difference -0.30 (95% CI -2.40 to 1.80), standardized effect d = -0.08; z-test p = 0.779.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Propofol and the control. The interval gives the range of effects that remain compatible with the data.

Systolic Blood Pressure

• 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:
  • Propofol: mean 126.00 versus 141.00 on control; difference -15.00 (95% CI -29.29 to -0.71), standardized effect d = -0.63; z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Propofol than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary measures cover several dimensions of hemodynamic response: refractory hypotension, episode duration, systolic and diastolic blood pressure, heart rate, and hormone concentrations. The posted quantitative comparisons include refractory hypotension, episode duration, and systolic blood pressure. The registry lists additional secondary outcomes, but their results are not reported in the registry record. This leaves the secondary picture incomplete rather than providing a comprehensive assessment across all listed measures.

Across the posted secondary comparisons, the estimates do not form a uniformly precise or statistically clear pattern. The refractory-hypotension estimate has an interval that spans zero, and the duration comparison also has an interval spanning zero. The systolic blood-pressure comparison has an interval below zero for propofol relative to methohexital. These different outcomes capture different features of response and should not be treated as interchangeable with the primary participant-level event count.

The secondary outcomes can provide context for the primary result, but they do not confirm it merely by pointing in a similar direction, nor do they overturn it when their estimates are uncertain or measure a different construct. The record does not report an adjustment for the many outcomes and comparisons. In general, testing multiple outcomes increases the chance that some results will appear noteworthy by chance if each is considered separately. Unadjusted secondary results therefore carry less confirmatory weight than a prespecified primary comparison, especially when the full analysis plan and results for all listed outcomes are not available in the registry record.

Repeated measurements of blood pressure and hormones may also require methods that account for the correlation of observations within a participant. The registry lists time points for some hormone measurements but does not report the model or the results for those outcomes. The available secondary findings are best viewed as limited, outcome-specific descriptive and inferential context, not a single combined verdict about all hemodynamic effects.

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

• Number of Participants With Refractory Hypotension
• Duration of Each Hypotension Episode
• Systolic Blood Pressure
• Diastolic Blood Pressure
• Heart Rate
• Serum Concentration of Norepinephrine (NE) (at Baseline (Time 0) and 3,5,10 and 15 Min After Anesthetic Induction)
• Blood Levels of Epinephrine (at Baseline (Time 0) and 3,5,10 and 15 Min After Induction of Anesthesia)
• Blood Levels of Angiotensin II (AII) (at Baseline (Time 0) and 3,5,10 and 15 Min After Anesthetic Induction)

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

In general, randomization assigns participants to groups by chance, which can help balance measured and unmeasured characteristics across groups on average. It does not guarantee identical groups, especially in a small study, and it does not address problems that occur after assignment, such as missing outcome data or deviations from the assigned intervention. The registry classifies this trial as randomized, but the sequence-generation method, concealment procedures, and handling of post-assignment deviations are not reported in the registry record.

What does the parallel, unmasked design mean?

In a parallel-group study, each participant is assigned to one intervention group for the comparison. This is distinct from a crossover design, in which participants receive multiple interventions in sequence. The registry identifies the study as parallel and unmasked. In general, lack of masking can influence behavior, care, or subjective outcome assessment, although the extent depends on the endpoint and study procedures. The primary outcome is a recorded hemodynamic event, but the registry does not detail assessment procedures or whether outcome assessors were independent of treatment assignment.

How should the event counts be understood?

The primary measure is a count of participants with an event, not a count of every episode. The posted arm values are 8 of 20 for methohexital and 21 of 25 for propofol. A proportion or risk describes the fraction of participants in an arm who experienced the event. The risk difference compares those arm-specific risks by subtraction; a positive value for propofol versus methohexital means the recorded event risk is higher in the propofol group on that scale. The unadjusted risk difference is 0.44. The risk ratio divides one arm's risk by the other's; the recalculated risk ratio is 2.1. These are different ways of expressing the same binary-outcome comparison and have different scales.

What is the role of the confidence interval and p-value?

In general, a confidence interval expresses uncertainty in an estimate under a specified statistical method. Its endpoints indicate which values are reasonably compatible with the observed data and assumptions at the stated confidence level. A p-value summarizes how unusual data at least as discrepant as those observed would be under a null hypothesis and model assumptions. Neither quantity replaces examination of the estimate, the outcome definition, and study quality. The recalculated risk-difference interval is 0.182 to 0.698, and its unadjusted p-value is 0.002. The registry separately reports a log-binomial regression p-value of 0.01 and a risk ratio value of 1, without a confidence interval.

What does log-binomial regression generally estimate?

Log-binomial regression is a model for binary outcomes that can estimate risk ratios when its assumptions and fitting conditions are met. The registry lists this method for the primary analysis and reports a risk ratio. The record does not state model covariates, diagnostics, missing-data handling, or further details of the fitted model. The recalculation uses posted summary counts and is unadjusted; it is not a reproduction of a model-based analysis.

Why do the secondary measures need separate interpretation?

Some secondary outcomes are binary counts, while others are means with standard deviations. These outcome types require different summaries and often different models. Repeated blood-pressure or hormone measurements can also be correlated within a participant. In general, repeated measurements are not independent observations, so analyses should account for their within-person relationship if that is the intended inferential target. The registry lists blood pressure, heart rate, and hormone measurements at specified times, but the statistical treatment of repeated measurements is not reported in the registry record.

For a continuous outcome, a mean difference describes the difference between group averages, while the standard deviation describes variability among observations within a group. A confidence interval for a mean difference expresses uncertainty in the group contrast. The posted secondary results include mean differences and intervals for duration of hypotension and systolic blood pressure. The calculations are unadjusted comparisons from summary statistics; they do not establish that all assumptions for a particular inferential model were checked.

Why can over-dispersion matter?

In general, over-dispersion occurs when outcome variability exceeds what a chosen statistical model expects. It can make standard errors too small if ignored, producing confidence intervals that are too narrow and p-values that are too optimistic. It is especially relevant for certain count models, where the model's assumed variance structure may not fit the data. The primary registry endpoint is described as a binary participant count, not a rate of repeated events, and dispersion is not reported for it. No claim about over-dispersion or diagnostic testing can be made from the registry record.

The record reports neither the trial's complete statistical analysis plan nor details of multiplicity control, missing-data methods, analysis populations, or interim monitoring. As general principles, these details help distinguish prespecified confirmatory analyses from exploratory comparisons and clarify the assumptions behind estimates. Their absence limits independent assessment of how closely the posted analyses follow the intended plan.

11. Confidence Intervals and Precision

The recalculated primary risk difference is 0.44, with a 95% confidence interval from 0.182 to 0.698. This interval excludes zero, so the unadjusted estimate is not compatible with equal event risks under the interval's method at its stated confidence level. The interval nevertheless spans a range of positive differences, rather than identifying one exact effect. Its width reflects uncertainty in the estimate and should be considered alongside the modest numbers of participants represented in the outcome groups.

The recalculated risk ratio is 2.1, with a 95% confidence interval from 1.196 to 3.689. A ratio interval is interpreted relative to 1, the value corresponding to equal risks. The interval lies above that reference value, but it still allows a range of magnitudes. The risk-difference and risk-ratio intervals describe the same comparison on distinct scales; neither should be read as a guarantee of the effect in a future study.

For the secondary refractory-hypotension comparison, the recalculated risk-difference interval runs from -0.105 to 0.305, spanning zero. The duration-of-hypotension mean-difference interval runs from -2.399 to 1.799, and the systolic blood-pressure mean-difference interval runs from -29.29 to -0.710. These intervals illustrate that precision differs across outcomes. A confidence interval that includes a null value does not prove that there is no difference; it indicates that the data and method remain compatible with values on both sides of that reference.

The registry does not report a confidence interval for its primary log-binomial regression result. Its reported p-value alone does not convey the range of plausible effect sizes. Confidence intervals also do not account for every limitation, such as outcome misclassification, missing data, model misspecification, or selective reporting. Those considerations require information beyond the interval calculation.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design justification. For these binary and continuous outcomes, the displayed figures are participants per arm; the rule for time-to-event outcomes would instead be total events, but the posted outcomes are not time-to-event outcomes. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the estimated participants per arm for a design that would have an 80% probability of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% power column gives the corresponding planning count for a higher chance of detection under those same assumptions. These are prospective planning concepts, not measures of how likely the completed trial was to find a result after its data were observed.

The rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more participants to distinguish them from random variation with the same target power and significance level. The resulting counts can differ greatly by endpoint because the observed effect and outcome variability differ. Very small observed effects can produce especially large planning estimates; that does not mean the trial enrolled those numbers or that its original investigators used these assumptions.

This is not observed power. It is a planning illustration calculated from the observed effect and stated assumptions. The trial's own sample-size calculation and original assumptions are not reported in the registry record. The curve should be read as a visual representation of the planning relationship between effect size and required participants per arm, not as an additional clinical result.

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 = 0.400; treatment proportion p₁ = 0.840; average p̄ = 0.620.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6864 = 1.3454.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6119 = 0.5150.
4. n = (1.3454 + 0.5150)² / (0.4400)² = 17.9, rounded up to 18 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 <- 0.4                          # control proportion
p1 <- 0.84                          # 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(2624050)
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 = 18 (80% power), 24 (90% power)
 75% of observed effect: n per arm = 35 (80% power), 46 (90% power)
 50% of observed effect: n per arm = 80 (80% power), 107 (90% power)
power.prop.test: 17.9 
Simulated power at n = 18 per arm: 0.830 (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 posts a sponsor-reported primary analysis using log-binomial regression. It lists a risk ratio value of 1 and p = 0.01, with no confidence interval. The registry does not provide the model's covariates, the precise coding or contrast behind the displayed value, or further explanation of the estimate.

A separate recalculation from the posted arm counts is unadjusted. It gives a risk difference of 0.44, a 95% confidence interval from 0.182 to 0.698, and p = 0.002; the recalculated risk ratio is 2.1, with a 95% confidence interval from 1.196 to 3.689. These figures are not the sponsor's fitted model output. They are a simple comparison based on the two reported event counts and group sizes.

The registry does not flag a discrepancy between the posted analysis and the recalculation. Still, the two sets of results should be kept distinct rather than combined or substituted for one another. The registry's analysis reflects the reported model, while the recalculation offers a transparent unadjusted comparison. Because the registry gives no confidence interval for its model estimate and little model detail, the precision and coding of that reported estimate cannot be independently evaluated from the record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome alongside numerous secondary outcomes and reports 3 analyses. It does not report whether the investigators adjusted for multiple comparisons, designated a hierarchy among secondary outcomes, or identified which secondary analyses were confirmatory. When many outcomes are tested, the chance of at least one apparently unusual result can increase even if no corresponding underlying effect exists. As a general statistical response, investigators may prespecify a hierarchy or use multiplicity-adjustment procedures, but whether either approach was used in this trial is not reported in the registry record.

Missing-data methods and participant disposition are also not reported in the registry record. The enrollment total is 51, while the posted primary endpoint groups include 20 participants in the methohexital arm and 25 in the propofol arm. The registry does not explain the difference between enrollment and the participants represented in those endpoint counts. Reasons could not be inferred from the record, and it does not state whether the displayed groups represent all randomized participants, an analyzed subset, or another analysis population.

The registry does not identify an intention-to-treat population, a per-protocol population, or rules for exclusions after randomization. It also does not describe imputation, complete-case analysis, or sensitivity analyses for missing outcomes. In general, the handling of missing observations can affect both estimates and uncertainty, particularly if missingness differs between groups or is related to outcome status. Without these details, the robustness of the posted comparison to missing data cannot be assessed.

Interim analyses, stopping rules, and any adjustment for repeated looks at the accumulating data are not reported in the registry record. Nor does the record provide the complete statistical analysis plan needed to determine which decisions were prespecified. These absences do not establish that particular procedures were or were not used; they limit what can be concluded from the registry entry about analysis conduct and the confirmatory status of the reported results.

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 0% reporting threshold.

The serious adverse event figures list zero serious adverse events in both posted safety groups: 0 among 25 participants for propofol and 0 among 20 participants for methohexital. The registry also lists zero deaths in each group and zero other adverse events in each group. No serious adverse event terms are listed.

These figures describe what was recorded in the registry for the participants represented in the safety groups. They do not establish that the interventions have no risk. In general, when no events are observed in a study, the data still allow for the possibility of uncommon events that were not observed in that sample. The limited group sizes and registry reporting also constrain how much can be learned about rare harms.

The record does not report detailed adverse-event definitions, surveillance procedures, duration of safety follow-up, or whether all randomized participants contributed to these safety counts. Those details are needed to interpret the scope and completeness of safety ascertainment. The zero counts should therefore be read as an absence of reported events in these registry groups, not as proof of absence of risk.

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

The posted primary counts show that hypotensive events were recorded more often in the propofol group than in the methohexital group during the stated induction period. The unadjusted recalculation quantifies that comparison as a risk difference of 0.44 and a risk ratio of 2.1, with confidence intervals that exclude their respective null values. This is a result about the observed participants, outcome definition, and analysis method, not a universal statement about anesthetic use.

The finding does not, on its own, establish the cause of every event or show how the result would apply to patients outside the registry population. The record does not provide detailed eligibility criteria, the operational definition of hypotension, complete participant flow, or the methods used to handle missing data. It also does not report the trial's original sample-size justification or full analysis plan. Those limitations leave important questions about generalizability and analytic robustness unresolved.

The registry's reported log-binomial analysis lists a risk ratio value of 1 and p = 0.01, while the separate unadjusted recalculation gives a risk ratio of 2.1. The record does not explain the displayed model estimate's coding or provide a confidence interval for it. These results should be recognized as separate outputs, not interpreted as interchangeable estimates. The recalculation does not replace the registry-reported analysis, and the registry result does not provide the same uncertainty information as the recalculated interval.

The secondary findings do not provide a complete or multiplicity-adjusted account across all listed outcomes. Some results are imprecise, and other listed secondary results are not reported in the registry record. The safety section records zero serious adverse events in the posted groups, but zero observed events do not demonstrate zero risk. Taken together, the trial offers a comparison of a narrowly defined early hemodynamic outcome, with uncertainty and reporting limitations that should remain part of any interpretation. It does not support medical advice or a conclusion extending beyond the trial's recorded data.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. For a binary outcome, the risk difference communicates an absolute contrast on the event-risk scale, while the risk ratio expresses a relative contrast. Both can be calculated from the same participant counts, yet their numerical values and interpretation differ. Reporting the estimate with a confidence interval gives more information than relying on a p-value alone.

It also demonstrates the distinction between a registry-reported model analysis and an unadjusted recalculation from summary data. The model may incorporate a specified structure or covariates, but the registry does not provide enough detail to reconstruct its reported result. A recalculation can make a simple comparison transparent, but cannot recover unreported modeling choices or participant-level data. Keeping those analyses separate is essential when their reported values differ in form or magnitude.

The trial further shows why a statistically noteworthy primary result does not resolve all questions about evidence strength. The registry records modest group sizes, additional outcomes, and no reported multiplicity approach, missing-data strategy, or original sample-size assumptions. These matters affect precision, selection of outcomes, and the degree to which secondary results can be treated as confirmatory. A result should be interpreted in the context of those design and reporting features rather than by a threshold alone.

Finally, planning calculations based on an observed effect are not a substitute for a prospective design rationale. The illustrations help readers understand how assumed effect size relates to planning requirements, but they do not reveal what investigators intended before the trial began. Distinguishing prospective planning from retrospective calculation prevents an observed result from being mistaken for evidence that a study was adequately powered for every outcome.

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.

The trial was unmasked, and the registry does not describe allocation concealment or independent outcome assessment. Although the primary endpoint is a recorded hemodynamic event, the threshold used to define hypotension and the rules for counting participants with multiple episodes are not reported in the registry record. These details affect reproducibility and may influence outcome classification.

The record gives an enrollment of 51, while the primary outcome groups contain 20 and 25 participants. It does not explain participant flow, the analysis population, or why the posted outcome counts do not account for the enrollment total. It also does not report missing-data methods or sensitivity analyses. Consequently, the relationship between randomized enrollment and the analyzed endpoint cannot be assessed from the registry entry.

The registry's model-based primary result is reported without a confidence interval or enough detail to understand its coding and specification. The recalculated estimate is unadjusted and based only on summary counts. Neither source provides enough information to check model assumptions or account for possible baseline imbalances. The registry does not report baseline characteristics or adjusted estimates.

Many secondary outcomes are listed, but results for some are not reported in the registry record, and multiplicity procedures are not described. The stated time points for hormone measurements also raise questions about repeated-measure analysis, which is not detailed. Finally, the trial's original sample-size rationale and broader eligibility criteria are not reported. These limitations constrain assessment of precision, selective reporting, analysis choices, and applicability beyond the recorded study groups.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Methohexital v Propofol as General Anesthetic in Patients on ACEIs or ARBs — NCT02624050.
• Registry record last updated 2025-01-28; status last verified 2025-01.
• Results first posted 2019-03-13.
• 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 describes a completed randomized, parallel-group, unmasked comparison of intravenous methohexital and propofol for anesthetic induction in patients treated with ACEIs or ARBs who were undergoing elective surgery. Enrollment was 51. The primary outcome was the number of participants with hypotensive events during the first 15 minutes of induction.

The posted primary counts were 8 of 20 in the methohexital group and 21 of 25 in the propofol group. The unadjusted recalculation gives a risk difference of 0.44 and a risk ratio of 2.1, with reported recalculated confidence intervals. The registry separately reports a log-binomial regression result with a risk ratio value of 1 and p = 0.01, without a confidence interval.

Secondary outcomes span event counts, episode duration, hemodynamic measures, and hormone concentrations. The registry lists zero serious adverse events and zero deaths in both posted safety groups. Details about the original sample-size rationale, missing data, multiplicity, and several analysis procedures are not reported in the registry record.