Evaluation of the Effect of Ketamine on Remifentanil-induced Hyperalgesia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Effect of Ketamine on Remifentanil-induced Hyperalgesia (NCT01301079), a randomized phase 3 study. The primary outcome is Pain 30 Minutes.

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, quadruple-masked, parallel-group Phase 3 study sponsored by the Federal University of São Paulo. The registered enrollment was 60. The posted primary outcome summaries list 28 participants in the ketamine group and 28 in the saline group. The registry record does not explain the relationship between the registered enrollment and the group sizes shown for this outcome.

The record lists a study start of 2010-09 and a primary completion of 2012-09. The intervention groups were ketamine and saline. Both arm descriptions include propofol, remifentanil, and atracurium in the anesthesia regimen, with atracurium titrated to maintain muscle relaxation. The descriptions are truncated, so the complete anesthesia protocols and the specific study-drug dosing cannot be established from the registry record.

The registry labels the study as randomized and quadruple-masked, but does not report the randomization sequence method, allocation concealment procedure, masking roles, or steps used to preserve masking. Eligibility criteria and participant characteristics are not reported in the registry record. It therefore offers limited information for judging how closely the enrolled group resembles any particular clinical population.

The trial's stated aim covered hyperalgesia, analgesia, and inflammatory markers. The primary posted endpoint is pain at 30 minutes. Secondary outcomes include morphine use and hyperalgesia assessments using monofilaments and an algometer at different locations or time points. The registry lists 36 outcome measures and 36 analyses, and 24 secondary results are posted. The original protocol, detailed statistical plan, and reasons for any differences in outcome availability 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

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 Pain 30 Minutes, measured over 30 minutes.

The primary endpoint is the mean pain score at 30 minutes. The registry describes a scale on which 0 means without pain and 10 means the worst pain possible; participants could choose any number between 0 and 10. Reporting the group mean and standard deviation summarizes both the average score and the spread of individual scores within each group.

Pain intensity is relevant to the stated study aim of assessing whether ketamine improves the analgesic effect associated with remifentanil and reduces remifentanil-induced hyperalgesia. A direct pain rating provides a patient-reported measure of pain at a specified assessment time. It is distinct from the other listed outcomes, such as morphine consumption and sensitivity measured with monofilaments or an algometer; those outcomes address related but non-identical aspects of postoperative pain and sensitivity.

The registry does not report why 30 minutes was selected, the exact assessment procedures, or whether additional pain scores contributed to the primary analysis. It also does not describe a clinically important difference for the scale. The posted group averages therefore describe measured pain scores, but by themselves do not establish how meaningful a difference would be to patients or clinicians.

7. Results Posted in the Registry

• Saline: mean 6.20 versus 5.50 on control; difference 0.70 (95% CI -0.91 to 2.31), standardized effect d = 0.23; z-test p = 0.396.

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.

Morphine Consumption Within 24 h

• 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:
  • Saline: mean 27.70 versus 27.40 on control; difference 0.30 (95% CI -7.99 to 8.59), standardized effect d = 0.02; z-test p = 0.943.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saline and the control. The interval gives the range of effects that remain compatible with the data.

Hyperalgesia in the Postoperative Period as Measured With Monofilaments in Thenar Eminence

• 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:
  • Saline: mean 247.00 versus 290.00 on control; difference -43.00 (95% CI -90.18 to 4.18), standardized effect d = -0.48; z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saline and the control. The interval gives the range of effects that remain compatible with the data.

Hyperalgesia in the Preoperative Period as Measured With Monofilaments in the Periumbilical Region

• 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:
  • Saline: mean 269.00 versus 279.00 on control; difference -10.00 (95% CI -54.46 to 34.46), standardized effect d = -0.12; z-test p = 0.659.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saline and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related but distinct questions: morphine use, time to first morphine supplementation, and sensitivity measured with monofilaments or an algometer at different locations and times. The registry lists 36 outcome measures and 36 analyses, with 24 secondary results posted. This breadth means that secondary outcomes provide a wider view of the study's measurements, but they do not all represent the same construct or time point.

The available quantitative summaries do not show a uniform pattern across these measures. The re-calculated comparison for morphine consumption is close to zero, while estimates for sensitivity vary in direction and precision. For postoperative thenar sensitivity, the sponsor-reported p-value is not the same as the simple re-calculation from the posted summaries. The registry record does not explain that difference. This mix does not provide a single consistent secondary signal that clearly reinforces the primary pain comparison.

Secondary results are generally less conclusive when many comparisons are examined without a reported adjustment for multiplicity. If each comparison is assessed separately, the chance of observing an apparently notable result by chance can increase across the set. The registry does not report whether multiplicity was addressed, which secondary outcomes were prespecified as confirmatory, or how the results should be ranked. Accordingly, secondary findings are best treated as context for the primary result rather than independent proof of a treatment effect.

The study aim also mentions interleukins, but cytokine outcome results are not reported among the posted summaries described in the registry record. The absence of those results from the available record does not establish whether they were measured, analyzed, or omitted. It limits the ability to assess how the inflammatory-marker aims relate to the pain and hyperalgesia findings.

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

• Time to First Morphine Supplementation
• Morphine Consumption Within 24 h
• Hyperalgesia in the Preoperative Period as Measured With Monofilaments in Thenar Eminence
• Hyperalgesia in the Postoperative Period as Measured With Monofilaments in Thenar Eminence
• Hyperalgesia in the Preoperative Period as Measured With Monofilaments in the Periumbilical Region
• Hyperalgesia in the Postoperative Period as Measured With Monofilaments in the Periumbilical Region
• Hyperalgesia in the Preoperative Period as Measured With Algometer in Thenar Eminence
• Hyperalgesia in the Postoperative Period as Measured With Algometer in Thenar Eminence

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary summaries give a mean and standard deviation for each group. A mean describes the average observed score, while the standard deviation describes how much individual scores vary around that average. The mean difference compares the two group averages. In this analysis, the difference is expressed as saline minus ketamine, so a positive estimate corresponds to a higher average pain score in the saline group. That sign convention is useful for reading the estimate, but does not itself establish a treatment effect.

A confidence interval gives a range of values compatible with the observed estimate under the assumptions of the calculation. It helps show precision: a narrow interval indicates greater precision than a wide one. For the primary endpoint, the interval extends from -0.915 to 2.315 and includes zero. The confidence level for the posted intervals is not reported in the registry record, so it should not be inferred from the numbers alone.

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. The registry reports a two-sided t-test for the primary comparison. A two-sided test considers evidence in either direction rather than only a prespecified increase or decrease. The registry does not report further details of its test implementation or any covariate adjustment.

The re-calculated comparisons are simple, unadjusted comparisons based on the posted group summaries. They are not replacements for the trial's own analysis. They do not account for participant-level data, adjustment variables, repeated measurements, or other modeling features that may have been used in an original analysis; whether such features were used is not reported in the registry record. Where sponsor-reported and re-calculated results differ, they should be presented separately rather than silently treated as interchangeable.

Why does dispersion matter?

Variation among participants affects how precisely group averages can be compared. When scores vary widely relative to the difference between averages, the data provide less precise evidence about the group contrast. The primary endpoint's standard deviations are 3.5 for ketamine and 2.6 for saline, while its confidence interval spans values on both sides of zero. This is why the difference in the observed averages should be read together with the variability and interval, rather than in isolation.

For continuous outcomes, an unadjusted mean difference is often an accessible summary, but it relies on interpreting the measure's numerical scale as meaningful for averages. The pain rating allows a participant to choose any number between 0 and 10. The registry does not report additional validation or analysis details for this scale in this trial. The mean summarizes the group-level distribution but does not show whether participants had similar experiences or whether scores clustered in particular parts of the scale.

What does over-dispersion mean in general?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if the model's variance assumptions are not appropriate. The posted summaries do not establish that over-dispersion was present or that a particular variance model was used. The concept is relevant as a general reminder that precision depends on how well the analysis accounts for the data's variability, not as a finding about this trial.

What can the planning calculations tell readers?

The sample-size illustrations use the observed effect as a starting point and consider detecting stated fractions of that effect. For continuous outcomes, the figures are participants per arm. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial's own sample-size assumptions and justification are not reported in the registry record. The illustrations are prospective planning scenarios, not a retrospective measure of whether the trial had adequate power.

General statistical planning depends on more than the observed difference alone. Variability, the effect chosen for planning, the allocation scheme, and the desired error rates all influence the number of participants needed. A calculation based on a trial's observed effect can be unstable, especially when that estimate is imprecise. Planning should therefore use a clinically justified target effect and suitable variance assumptions rather than treating an observed estimate as a guaranteed future effect.

The registry's own analysis plan is not reported in the registry record. In particular, it does not establish whether the primary analysis followed intention-to-treat principles, how missing observations were handled, whether baseline adjustment was planned, or whether any interim analyses occurred. Those details matter when interpreting the p-values and when assessing whether the posted results correspond to the intended analysis.

11. Confidence Intervals and Precision

The primary mean difference is 0.7 units, with a confidence interval from -0.915 to 2.315. Its width indicates that the estimated contrast is not highly precise. The interval includes zero and includes values favoring either group under the stated saline-minus-ketamine direction. Thus, the observed means alone do not pin down the size or direction of a population difference with much certainty.

Confidence intervals are useful because they show a range of effect estimates compatible with the data and the calculation assumptions. They are not a list of values that each have a particular probability of being true. Their interpretation depends on the statistical method and confidence level. The registry does not report the confidence level or the method used to construct these intervals, so those features cannot be specified from the record.

The confidence interval is also different from a p-value. A p-value condenses evidence relative to a null hypothesis, whereas an interval communicates both direction and a range of effect sizes. Here the sponsor-reported primary p-value is 0.386, and the simple unadjusted re-calculation gives 0.396. Both should be read alongside the interval and the group summaries rather than as stand-alone verdicts.

For secondary outcomes, precision varies across measures. Some intervals are broad relative to their estimates, and a sponsor-reported p-value for one hyperalgesia comparison does not match the re-calculation from the posted summaries. The registry does not explain the difference. That uncertainty, together with the number of secondary outcomes, limits how confidently an isolated secondary result can be interpreted. The precision of a statistical estimate also does not determine whether the effect is clinically important; a threshold for meaningful change is not reported in the registry record.

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 for continuous outcomes are participants per arm, not a combined group total. If a planning calculation concerns a time-to-event outcome, its figures represent total events; the listed outcomes with these continuous-measure calculations use participants per arm. The illustrations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect.

The 80% power column describes the number of participants per arm the calculation estimates would be needed for an 80% chance of detecting the specified effect if that effect and the planning assumptions were true. The 90% power column uses a higher target chance of detection and consequently gives a larger planned group size. These are conditional design calculations, not guarantees: actual power depends on the true effect, variability, analysis, and adherence to assumptions.

The rows planning for 100% of the observed effect use the full observed estimate as the target; rows for 75% or 50% use smaller target effects. Detecting a smaller difference generally requires more participants, all else equal. This pattern is reflected in the planning figures. The calculations are illustrations based on the observed effect, not the trial's original design justification. The trial's original sample-size assumptions are not reported in the registry record. These figures are not observed power.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.700; pooled standard deviation σ = 3.083.
2. n = 2 × (1.96 + 0.842)² × 3.083² / 0.700² = 304.5, rounded up to 305 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
delta <- 0.7                      # observed difference in means
sigma <- 3.0830180018936                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1301079)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 305 (80% power), 408 (90% power)
 75% of observed effect: n per arm = 542 (80% power), 725 (90% power)
 50% of observed effect: n per arm = 1,219 (80% power), 1,631 (90% power)
power.t.test: 305.5 
Simulated power at n = 305 per arm: 0.796 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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

For the primary pain outcome, the registry reports a two-sided t-test with p = 0.386. The simple unadjusted re-calculation from the posted means, standard deviations, and group sizes gives p = 0.396, with a mean difference of 0.7 units and a confidence interval from -0.915 to 2.315. The close p-values indicate that the simple comparison gives a broadly similar statistical reading, while the registry's own analysis remains the trial-reported result.

The registry does not provide enough detail to reconstruct the sponsor's analysis beyond identifying the t-test as two-sided. It does not give a sponsor-reported effect estimate or confidence interval for the primary result. The re-calculated interval is therefore useful as a transparent summary from the posted group statistics, but it should not be represented as the sponsor's interval.

For a postoperative thenar monofilament comparison, the sponsor-reported p-value differs from the unadjusted re-calculated p-value. The registry record does not explain the difference, and it does not give enough analytical detail to determine its source. The two results should be kept distinct: the sponsor's analysis is the reported trial analysis, while the re-calculation is a simple comparison derived from summary statistics. Neither should be substituted for participant-level analysis or a fuller protocol-based interpretation.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a broad set of outcome measures and analyses, with 24 secondary results posted. When many outcomes are tested, interpreting each p-value as if it were the only planned test can overstate the strength of isolated findings. Multiplicity methods, such as adjusting the testing threshold or controlling an error rate across outcomes, can address this issue, but the registry does not report whether any such method was used.

The record identifies the primary outcome as pain at 30 minutes, but it does not include a full statistical analysis plan or explain how the primary and secondary hypotheses were prioritized. The original protocol and prespecification details are not reported in the registry record. It is therefore unclear whether all listed outcome measures were planned before data collection, whether any were exploratory, or whether outcome definitions changed.

Missing-data handling and analysis populations are also not reported in the registry record. The posted primary group summaries include 28 participants per arm, while registered enrollment is 60, but the record does not explain the relationship between those figures. It does not state whether all randomized participants were included in the analysis, whether exclusions occurred, or how missing observations were addressed. No reason for any difference in outcome availability should be inferred.

The registry does not report whether the primary analysis was intention-to-treat, per-protocol, or another defined analysis population. It also does not state whether covariates or baseline values were included, how repeated or correlated measurements were modeled, or whether interim analyses were conducted. These omissions do not invalidate the posted results, but they restrict assessment of whether the analysis followed the planned strategy and how robust the findings are to alternative assumptions.

These gaps matter especially for secondary comparisons, where selective availability and multiplicity can influence interpretation. The primary result is more clearly identified, but details about its population, missing data, and model remain incomplete. A protocol and full analysis plan would be needed to resolve these questions.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list 0 affected among 28 at risk in the ketamine group and 0 affected among 28 at risk in the saline group. The registry lists no serious adverse event terms. These entries describe the serious-event counts recorded for the groups shown; they do not establish that no serious events occurred outside the recorded population or observation period.

The registry also records other adverse events affecting 16 participants in the ketamine group and 8 in the saline group. The record does not provide event-level descriptions, severity breakdowns, or a statistical comparison in the information. Those counts should not be interpreted as evidence that one treatment is safer, since the types and clinical significance of the events are not specified.

Deaths are not reported in the registry record. The observation period and the completeness of adverse-event ascertainment are also not reported. Safety interpretation is therefore limited to the event counts and denominators entered in the record; a fuller assessment would require definitions, event descriptions, timing, and information about follow-up.

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

The primary estimate describes average pain scores at 30 minutes in the two posted groups. The saline group mean was 6.2 and the ketamine group mean was 5.5, yielding an unadjusted mean difference of 0.7 units when expressed as saline minus ketamine. The interval from -0.915 to 2.315 includes zero and spans both directions. The result therefore does not determine a clear difference in average pain between groups.

This is not the same as proving that the groups are equivalent. An interval that includes zero can still include effects that matter, and the registry does not report a clinically important difference for the pain scale. Nor does the result establish that ketamine has no effect. The estimate is uncertain, and the available summary does not resolve how large or in which direction a population-level difference may be.

The study's stated aims include reducing remifentanil-induced hyperalgesia, improving analgesia, and evaluating inflammatory cytokines. The posted primary result addresses pain at a specified time, not every part of those aims. Secondary measures and cytokine results have different meanings and levels of availability. The record's outcome summaries cannot be treated as a complete account of all biological or clinical effects.

Randomization and masking are important design features, but the registry's abbreviated reporting does not allow a full assessment of how they were implemented or how missing observations were handled. The results should be interpreted as the estimates recorded for this trial, not as a universal prediction for every patient, procedure, or anesthesia regimen. No advice about treatment choice follows from these statistical summaries alone.

18. Why This Trial Matters Statistically

This trial illustrates why a group difference should be interpreted with its uncertainty rather than by comparing averages alone. The observed primary means differ, but the interval includes zero and covers values in both directions. The estimate and its precision answer related but distinct questions: the estimate gives the observed contrast, while the interval shows how much uncertainty surrounds it under the calculation assumptions.

It also demonstrates the difference between a trial-reported analysis and a simple re-calculation from summary statistics. For the primary endpoint, the sponsor-reported and re-calculated p-values are close. For one secondary comparison, they differ. Without more detail about the sponsor's analysis, the summary-based calculation cannot explain or replace the reported analysis. Keeping those results separate makes the evidence easier to audit.

The study's many outcome measures highlight the statistical challenge of interpreting secondary findings. Multiple tests can produce isolated results that appear notable even when there is no consistent pattern. Clear prioritization, prespecified analysis methods, multiplicity handling, and transparent reporting would help readers distinguish confirmatory evidence from exploratory signals. Those details are not reported in the registry record.

Finally, planning calculations based on an observed effect are useful as illustrations of how target effect size and desired power affect sample requirements. They are not evidence of the trial's original design reasoning or its observed power. This distinction helps prevent retrospective calculations from being mistaken for a verdict on whether the study was adequately designed.

19. Limitations

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

Several limitations specific to the available registry record constrain interpretation. The primary outcome summaries show 28 participants per arm, whereas registered enrollment is 60; the record does not explain the relationship. The analysis population, participant flow, exclusions, and missing-data procedures are not reported. As a result, the basis for the posted group summaries cannot be fully assessed.

The trial is described as randomized and quadruple-masked, but the randomization procedure, concealment, masking roles, and assessment of masking are not reported. Eligibility criteria and participant characteristics are also absent, limiting assessment of the study population and generalizability. The arm descriptions are truncated, and the ketamine and saline dosing details are not reported in the registry record.

The primary endpoint is a single pain assessment at 30 minutes, and the registry does not report why this timing was selected, a clinically important difference, or additional details of scale administration. The record identifies a two-sided t-test but does not provide a complete statistical analysis plan, confidence-interval level, or participant-level analysis details. The sponsor-reported analysis for one secondary comparison differs from the simple re-calculation, with no explanation in the record.

The outcome set is broad, while only 24 secondary results are posted. Multiplicity handling and prespecification of secondary hypotheses are not reported. Results for the interleukins named in the study aim are not included in the available summaries. Adverse-event entries lack event-level descriptions and follow-up details, and death counts are not reported. These limitations reflect gaps in the registry record and should not be treated as proof that particular procedures or analyses were absent from the conducted study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Effect of Ketamine on Remifentanil-induced Hyperalgesia — NCT01301079.
• Registry record last updated 2014-11-10; status last verified 2014-10.
• Results first posted 2014-11-10.
• 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.

23. Record Summary

The registry record describes a completed, randomized, quadruple-masked, parallel-group Phase 3 study sponsored by the Federal University of São Paulo, with ketamine compared with saline. Registered enrollment is 60, and the primary posted outcome is pain at 30 minutes on a 0-to-10 scale.

The primary group means are 5.5 for ketamine and 6.2 for saline. The unadjusted re-calculated mean difference is 0.7 units, with a confidence interval from -0.915 to 2.315; the sponsor-reported two-sided p-value is 0.386. The interval includes zero and permits uncertainty in either direction.

Secondary outcomes cover morphine use and hyperalgesia measures, with mixed estimates and incomplete reporting. The registry does not report key details about the analysis plan, missing data, multiplicity handling, or the full intervention protocols. These gaps limit how far the posted results can support conclusions about the study's broader aims.