Ketamine for Postoperative Avoidance of Depressive Symptoms: The K-PASS Feasibility Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ketamine for Postoperative Avoidance of Depressive Symptoms: The K-PASS Feasibility Trial (NCT05233566), a randomized phase 3 study. The primary outcome is Fraction of Approached Patients Who Enroll and Are Randomized.

2. Clinical Question

3. Trial Design

The K-PASS study is registered as a completed phase 3, randomized, quadruple-masked, parallel trial sponsored by Washington University School of Medicine. The registry lists an enrollment of 32. The recorded study start is 2022-04-25, and the primary completion date is 2023-03-08. Its brief summary describes a feasibility trial intended to evaluate whether a full-scale phase 3 trial could be conducted to test the postoperative ketamine hypothesis.

The intervention was ketamine and the control was normal saline. Both were administered following surgery and extubation; the saline was given at an equal rate to the ketamine regimen. The registry identifies the clinical condition as postoperative depression. It also lists depressive symptoms on Day 4 and delta sleep ratio on Night 1 following study medication among the secondary outcomes, including stratified delta sleep ratio outcomes by sex and race.

The primary endpoint is a recruitment measure: the fraction of approached patients who enrolled and were randomized. The posted result is organized by Protocol Version 1 and Protocol Version 2. The record does not explain the relationship between these protocol-version groups, the registry enrollment figure, and assignment to ketamine or control. Consequently, the primary comparison should not be read as a randomized comparison of the study drugs. The registry lists 15 outcome measures and four posted secondary outcomes, but detailed results for those secondary outcomes are not reported in the registry record.

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

Analysis population for the primary outcome, as defined in the registry: The analysis population for this outcome includes all patients who were approached by the research team, including those who decided not to participate in the trial and those who were excluded from the trial prior to randomization. Because these patients were never randomized, it is not possible to report results for this outcome separately for the Ketamine Arm and the Control Arm.

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 Fraction of Approached Patients Who Enroll and Are Randomized, measured over 3 days after surgery.

The primary endpoint measures recruitment feasibility rather than a clinical outcome. Its numerator includes patients randomized to receive either ketamine or placebo; its denominator includes all patients approached by the research team to evaluate eligibility and offer consent. The analysis population is therefore broader than the randomized population: it includes people who declined participation and people excluded before randomization. The stated timeframe is 3 days after surgery.

For a feasibility study, this type of endpoint can indicate whether the research team is able to approach patients and enroll and randomize them. It can inform the practical prospects of conducting a larger trial, while not establishing whether the treatment changes depressive symptoms. The posted result reports 1 randomized participant among 27 approached in Protocol Version 1 and 31 among 101 approached in Protocol Version 2. These are protocol-version groups, not the randomized ketamine and saline arms, so the comparison addresses recruitment under the two recorded versions rather than a treatment effect.

The registry record does not report why the protocol versions differ, how patients were assigned to a version, or how the relationship between these version-specific counts and the registry enrollment of 32 should be interpreted. Those details matter when assessing the endpoint and its generalizability.

7. Results Posted in the Registry

• Protocol Version 2: 30.7% (31/101) versus 3.7% (1/27) on control; risk difference 27.0 percentage points (95% CI 15.5 to 38.5), risk ratio 8.29 (1.18–57.99); unadjusted two-proportion z-test p = 0.004.

8. Statistical Interpretation

9. Statistical Methods Explained

The central statistical distinction is between a feasibility endpoint and a clinical efficacy endpoint. Here, the primary endpoint is the fraction of approached patients who enrolled and were randomized. It is a binary outcome at the participant level: each approached patient either reached randomization or did not. The posted group counts are expressed as 1 of 27 for Protocol Version 1 and 31 of 101 for Protocol Version 2. The registry defines the denominator to include patients who declined and patients excluded before randomization, not only randomized participants.

What does a risk difference describe?

A risk difference compares the event proportions in two groups by subtracting one proportion from the other. In this setting, the event is enrollment and randomization among approached patients, and the groups are protocol versions. A positive contrast in the direction of Protocol Version 2 means that the recorded recruitment proportion was higher for that version. It is an absolute measure, but it remains a comparison of protocol versions; it is not a ketamine-versus-saline treatment effect. The registry reports a risk-difference estimate and an interval, but the exact endpoints are not repeated.

How do the relative measures differ?

A risk ratio compares the event proportions as a ratio, while an odds ratio compares the odds of the event. Both express relative contrasts and can look numerically different from an absolute risk difference. The posted risk ratio is 8.287, with a confidence interval from 1.184 to 57.99. The posted odds ratio is 11.51, with a confidence interval from 1.495 to 88.69. These values concern enrollment and randomization across the protocol versions. They should not be interpreted as relative changes in postoperative depression or as estimates of the drugs’ effects.

What does the p-value tell the reader?

The posted comparison includes an unadjusted p-value of 0.004. In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions used for that test. It is not the probability that the null hypothesis is true, does not measure the size or clinical importance of a difference, and does not explain why groups differ. Because this result is a protocol-version comparison, the p-value pertains to that recruitment comparison. Adjustment for other variables is not reported in the registry record.

Why can a large relative estimate still be uncertain?

Confidence intervals describe the range of effect values that are reasonably compatible with the data and the analysis assumptions. A wide interval indicates limited precision: although the estimated direction may be clear, the underlying magnitude could vary substantially. The intervals for the relative measures extend from values closer to no contrast to much larger values. This is consistent with uncertainty about the magnitude of the recruitment difference. Statistical evidence against a null contrast and precision about the size of the contrast are related but distinct considerations.

What is over-dispersion, and does it apply?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It can matter for count outcomes when a model assumes a particular amount of variability, because underestimated variability can make uncertainty appear too small. The primary outcome is reported as counts of participants with an event, not as a repeated or rate-based count process, and the registry does not report a model-based over-dispersion analysis. It would therefore be inappropriate to claim that over-dispersion was tested or handled in the primary analysis. The record also does not report a detailed statistical plan or an adjusted model.

The trial’s randomized, masked, parallel design describes the intended treatment comparison between ketamine and saline. The posted primary endpoint result instead compares protocol versions. Design features of the drug trial cannot by themselves make that version comparison equivalent to a randomized treatment comparison. To assess the relationship between the two, a reader would need information about protocol-version assignment and implementation; these details are not reported in the registry record.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. A confidence interval gives a range of values compatible with the observed data under the analysis assumptions; it does not guarantee that the true value lies inside that range, and it is not a range of individual patient outcomes. Narrower intervals generally indicate greater precision, while wider intervals indicate more uncertainty about the size of an effect.

The posted risk-ratio interval runs from 1.184 to 57.99, and the odds-ratio interval runs from 1.495 to 88.69. Both intervals are wide, particularly toward their upper bounds. They therefore leave substantial uncertainty about the magnitude of the relative recruitment contrast between Protocol Version 2 and Protocol Version 1. The lower bounds are above the null value of 1 for these ratio measures, but that does not remove the uncertainty about how large the contrast is. The risk-difference interval is also reported in the registry results, but its bounds are not repeated in this explanation.

The unadjusted p-value of 0.004 addresses evidence against a null comparison under the test assumptions; it is not a substitute for examining the interval. A result can have a small p-value while still having an imprecisely estimated effect size. In this case, interpretation is further limited because the comparison is between protocol versions and the record does not explain their assignment or implementation. The intervals describe statistical uncertainty in the posted comparison; they do not account for unreported design details or establish a causal explanation for the observed difference.

11. 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 participants per arm, not total events. They are illustrative calculations based on the observed recruitment effect, rather than the trial’s original design assumptions. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions.

For planning for 100% of the observed effect, the figures are 30 participants per arm for 80% power and 39 participants per arm for 90% power. For planning for 75% of the observed effect, they are 45 participants per arm for 80% power and 59 participants per arm for 90% power. For planning for 50% of the observed effect, they are 80 participants per arm for 80% power and 106 participants per arm for 90% power.

In general, power is the chance that a study will detect an effect of the specified size under the assumptions of its calculation. The 80% column gives the planning size associated with an 80% chance of detecting that assumed effect; the 90% column gives the size associated with a 90% chance. Smaller effects require more participants to detect with the same power, which is why the illustrative participant counts increase as the assumed fraction of the observed effect decreases. These figures are not observed power; they are planning illustrations and should not be treated as a design recommendation without considering the trial question and assumptions.

12. 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 = 0.037; treatment proportion p₁ = 0.307; average p̄ = 0.172.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5337 = 1.0460.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4984 = 0.4195.
4. n = (1.0460 + 0.4195)² / (0.2699)² = 29.5, rounded up to 30 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 <- 0.037037037037037                          # control proportion
p1 <- 0.306930693069307                          # 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(5233566)
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 = 30 (80% power), 39 (90% power)
 75% of observed effect: n per arm = 45 (80% power), 59 (90% power)
 50% of observed effect: n per arm = 80 (80% power), 106 (90% power)
power.prop.test: 29.5 
Simulated power at n = 30 per arm: 0.861 (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.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, or analyses are tested. In general, conducting many tests can increase the chance of at least one apparently notable result by chance. The registry lists 15 outcome measures and identifies four secondary outcomes: depressive symptoms on Day 4, delta sleep ratio on Night 1 following study medication, and delta sleep ratio outcomes stratified by sex and race. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting these outcomes. It also does not report numerical results for these secondary outcomes in the information.

The primary comparison has an unadjusted p-value of 0.004. The record does not state whether this comparison was one of several planned tests, whether any adjustment was applied, or how the analysis relates to a prespecified analysis plan. The number of outcome measures alone does not establish that all were tested or that a correction was required; the testing plan is not reported in the registry record.

Missing-data handling is also not reported in the registry record. For the primary endpoint, the denominator is defined as all patients approached, including those who declined participation and those excluded before randomization. That definition clarifies which patients belong in the recruitment denominator, but it does not explain how incomplete approach records, unavailable eligibility information, or other missing observations were handled. Missing-data rules for secondary outcomes are not reported.

The registry describes the primary analysis population broadly, but analysis populations for the secondary outcomes and treatment-arm comparisons are not reported in the registry record. The record does not state whether an intention-to-treat, per-protocol, or other analysis population was used for clinical outcomes. These omissions limit assessment of whether all randomized participants were analyzed as assigned and how incomplete outcome measurements may affect the results. No interim analyses or detailed statistical analysis plan are reported in the registry record.

14. 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: seizure (6.2%), ramsay hunt syndrome (6.2%), postoperative apnea (6.2%), subjective arm/leg weakness (6.2%), surgical site infection (6.2%).

The safety record reports serious adverse events for 2 of 16 at risk in the ketamine arm and 5 of 16 at risk in the control arm. Other adverse events are reported for 0 of 16 at risk in the ketamine arm and 3 of 16 at risk in the control arm. The recorded deaths are 0 in the ketamine arm and 1 in the control arm. These are descriptive counts; the registry information does not establish that an event was caused by study medication.

The listed serious adverse-event terms each have a reported frequency of 6.2%: Seizure, Ramsay Hunt syndrome, Postoperative Apnea, Subjective arm/leg weakness, Surgical Site Infection, and Deep Venous Thrombosis. The record does not give enough detail in these entries to assign each listed term to a treatment arm or to infer how event terms relate to the participant-level serious-event counts. They should therefore be read as reported safety listings, not as comparative rates for a particular arm.

Safety counts in a feasibility trial are descriptive and do not by themselves establish comparative risk. The registry record does not report further detail about severity, timing, relatedness, or statistical comparisons for these events.

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

The result does show a difference in the recorded primary recruitment outcome between Protocol Version 1 and Protocol Version 2. The counts are 1 randomized participant among 27 approached in Protocol Version 1 and 31 among 101 approached in Protocol Version 2. The comparison has an unadjusted p-value of 0.004. The ratio estimates and their wide intervals indicate that the relative magnitude of the recruitment contrast remains uncertain.

The result does not show that ketamine prevents postoperative depressive symptoms. The primary endpoint is the fraction of approached patients who enrolled and were randomized, and the comparison is by protocol version rather than by ketamine and saline treatment arms. Although the trial’s stated hypothesis concerns postoperative depressive symptoms, the primary result is not a symptom outcome. Numerical results for the listed secondary depressive-symptom and sleep outcomes are not reported in the registry record.

Nor does the comparison establish why recruitment differed between versions. The record does not report how the versions were assigned or implemented, or how their counts relate to the registry enrollment of 32. Without those details, the version contrast cannot be attributed to a particular change or interpreted as a causal effect of a protocol modification.

The finding is best read as a recruitment-feasibility observation that may be relevant to planning further research. Its scope is limited to the recorded approached-patient denominators and randomized-participant numerators. It is not evidence about clinical benefit, lack of benefit, or comparative safety. The safety entries are descriptive counts, and the record does not establish event attribution. Further interpretation of the clinical outcomes would require results and analysis details not reported in the registry record.

16. Why This Trial Matters Statistically

This trial is statistically notable because its primary endpoint addresses whether a study can recruit and randomize patients, while the scientific hypothesis concerns postoperative depressive symptoms. Separating feasibility outcomes from clinical outcomes prevents a recruitment finding from being mistaken for evidence about treatment efficacy. In this record, that distinction is especially important because the posted primary comparison is organized by protocol version rather than by randomized treatment arm.

The endpoint also illustrates how denominator definitions shape interpretation. It includes all approached patients, even those who declined or were excluded before randomization. That makes the outcome relevant to the recruitment pathway, rather than only to the experience of participants who entered the randomized trial. At the same time, meaningful interpretation depends on understanding how patients were approached and how the protocol versions were used, details not reported in the registry record.

Finally, the posted relative estimates have wide confidence intervals. That emphasizes why statistical significance and precision answer different questions: the p-value describes evidence against a null contrast under the analysis assumptions, whereas the interval communicates uncertainty about the size of that contrast. A feasibility result can be useful for planning, but it should not be translated into a clinical treatment claim. The distinction among recruitment, treatment effect, and safety is central to reading this record accurately.

17. 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 primary comparison is reported between protocol versions, while the registry’s trial design describes randomized ketamine and saline arms. The record does not explain how protocol versions were assigned, what changed between them, or how the version groups relate to treatment assignment. This limits causal interpretation of the recruitment contrast. The registry lists enrollment of 32, while the primary endpoint reports approached-patient denominators of 27 and 101 by version; the relationship among these figures is not explained in the registry record.

The endpoint measures enrollment and randomization, not depressive symptoms. Although depressive symptoms on Day 4 are listed as a secondary outcome, numerical secondary results are not reported in the registry record. The same applies to the listed delta sleep ratio outcomes. The record therefore does not support an assessment of the stated clinical hypothesis from these results alone.

The relative-effect confidence intervals are wide, so the magnitude of the recruitment contrast is uncertain. The comparison is unadjusted, and the registry record does not report an adjusted analysis, multiplicity plan, detailed statistical analysis plan, missing-data procedures, interim analyses, or the original sample-size justification. The planning illustrations are based on the observed effect and are not the trial’s original design assumptions.

The safety entries are counts and listed event terms. Further information about event timing, severity, relatedness, and allocation of the listed terms by arm is not reported in the registry record. These limitations require cautious, descriptive interpretation and preclude treating the recruitment comparison as evidence of a clinical treatment effect.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Ketamine for Postoperative Avoidance of Depressive Symptoms: The K-PASS Feasibility Trial — NCT05233566.
• Registry record last updated 2026-08-21; status last verified 2024-03.
• Results first posted 2024-04-10.
• 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.

21. Record Summary

NCT05233566 is the completed K-PASS feasibility trial, sponsored by Washington University School of Medicine and registered as phase 3. It is described as randomized, quadruple-masked, and parallel, with ketamine and normal saline arms. The registry enrollment is 32; the study start is 2022-04-25 and primary completion is 2023-03-08.

The primary endpoint is the fraction of approached patients who enrolled and were randomized, with a timeframe of 3 days after surgery. The posted comparison is by protocol version: 1 of 27 for Protocol Version 1 and 31 of 101 for Protocol Version 2. This is a recruitment result, not a ketamine-versus-saline comparison or a depressive-symptom treatment effect. The registry lists four secondary outcomes, but their numerical results are not reported in the registry record.