Effect of Spinal Ketorolac After Acute Opioid Exposure: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Spinal Ketorolac After Acute Opioid Exposure (NCT00693160), a randomized phase 2 study. The primary outcome is Hyperalgesia.

2. Clinical Question

The registry's stated interests include the effect of remifentanil on the capsaicin-associated painful skin area and the pain-relieving effects of spinal ketorolac when given with intravenous remifentanil. The posted arm descriptions define the randomized contrast more narrowly: both groups received remifentanil and capsaicin, while the intrathecal injection differed. Thus, the posted primary comparison addresses the added effect associated with ketorolac relative to placebo in this experimental setting; it does not compare remifentanil with no remifentanil.

The study was conducted in healthy participants using an induced hypersensitivity model. It can therefore describe responses under those experimental conditions, but the registry results do not directly establish what would happen in clinical pain after surgery, trauma, or nerve injury. The record does not report a separate comparison that isolates remifentanil's effect.

3. Trial Design

The registry describes NCT00693160 as a phase 2, randomized, triple-masked, parallel-group study sponsored by Wake Forest University. Enrollment was 30. The recorded start was 2007-12, primary completion was 2010-10, and the study status is terminated. The reason for termination is not reported in the registry record.

Participants were assigned to intrathecal ketorolac or placebo intrathecal injection. Both arm descriptions specify remifentanil exposure and the topical capsaicin model for hypersensitivity and allodynia assessment. The ketorolac arm received a single intrathecal injection of ketorolac 2 mg; the comparator arm received a single injection of preservative-free normal saline. The record identifies the design as parallel, so the reported arms represent separate groups rather than a stated crossover comparison.

Randomization indicates assignment by chance, but the sequence-generation method, concealment procedures, and allocation ratio are not reported in the registry record. Triple masking is recorded, but which roles were masked and how masking was maintained are not reported. The registry lists healthy participants as the condition and does not identify a clinical patient population in the posted arm descriptions.

The primary outcome was mean total area of hypersensitivity, with standard deviation as the measure of spread, assessed approximately 24 hours after injection. The secondary outcome was cerebrospinal-fluid PGE2 concentration, also reported as a mean and standard deviation, at 2.5 hours. The registry lists two outcome measures, one posted secondary outcome, and no reported analyses. The protocol's original sample-size justification, planned allocation details, and analysis plan are not reported in the registry record. The terminated status alone does not explain why the trial ended or whether termination affected the planned analyses.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Hyperalgesia, measured over 24 hours.

The primary endpoint is total area of hypersensitivity, recorded in centimeters^2, assessed approximately 24 hours after intrathecal ketorolac injection. The registry describes use of a von Frey filament to assess the sensitive area. The outcome is continuous: each participant's measurement can take a range of values, and the posted arm summaries are means with standard deviations.

In this experimental model, capsaicin cream was used to elicit a sunburn-like skin sensation and associated hypersensitivity or allodynia. Measuring the area provides a way to quantify the spatial extent of the induced response rather than relying only on a verbal description of sensation. The endpoint is therefore relevant to the study's mechanistic question about skin sensitivity following acute opioid exposure and the possible contribution of intrathecal ketorolac.

The measurement is a surrogate experimental response, not a direct measure of pain relief after surgery or nerve injury. The registry's own summary describes the capsaicin sensation as similar to, but much milder than, pain in those clinical contexts. The record does not report further measurement details, such as the exact filament testing procedure, assessor training, repeatability, or a threshold for a clinically meaningful difference. Those omissions limit interpretation of what a change in measured area would mean beyond this model.

7. Results Posted in the Registry

• Intrathecal Ketorolac: mean 70.10 versus 48.40 on control; difference 21.70 (95% CI -5.12 to 48.52), standardized effect d = 0.59; z-test p = 0.113.

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.

Cerebrospinal Fluid (CSF) Prostaglandin E2 (PGE2) Concentration

• 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:
  • Intrathecal Ketorolac: mean 87.00 versus 75.00 on control; difference 12.00 (95% CI -47.63 to 71.63), standardized effect d = 0.18; z-test p = 0.693.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intrathecal Ketorolac and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists cerebrospinal-fluid PGE2 concentration as the secondary outcome, measured at 2.5 hours. Its posted comparison is uncertain, with a confidence interval that includes zero and an unadjusted p-value that does not provide strong evidence against a null difference. The secondary arm summaries also show substantial variability, particularly in the ketorolac arm. These features make the secondary estimate imprecise and limit how much weight it can carry.

The secondary outcome offers a related but distinct perspective from the primary hypersensitivity measure. PGE2 concentration is a biological measurement, while the primary endpoint is an area of induced skin sensitivity. A pattern in one does not necessarily establish a corresponding pattern in the other, and the registry does not report a mediation analysis linking PGE2 to hypersensitivity. The results therefore cannot establish whether the secondary measure explains the primary response or supports a common mechanism.

The secondary comparison does not overturn or resolve the uncertainty in the primary result. Both outcomes are reported as continuous measures with mean differences and uncertainty intervals, but they address different dimensions of the experiment and were assessed at different times. The posted results do not report a prespecified hierarchy for interpreting the secondary measure alongside the primary endpoint.

Unadjusted secondary results carry less weight because multiple outcomes create more opportunities for apparently notable findings even when the underlying effects are absent. A multiplicity adjustment or a prespecified testing hierarchy can address that issue, but neither is reported in the registry record. The secondary outcome should consequently be treated as exploratory evidence rather than as an independent confirmation of the primary comparison. The registry does not report additional secondary analyses that could clarify the pattern.

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

• Cerebrospinal Fluid (CSF) Prostaglandin E2 (PGE2) Concentration

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports a mean and standard deviation for each arm. A mean describes the average measurement within an arm. The standard deviation describes the spread of individual measurements around that average; it is not the uncertainty of the mean itself. Here, the reported spread is sizable in both arms, indicating that individual hypersensitivity areas varied considerably within each group.

The comparison is a mean difference: the ketorolac-arm mean minus the placebo-arm mean. The posted estimate is 21.7 centimeters^2. A positive estimate in this direction means the average measured area was larger in the ketorolac arm in the observed sample. The sign alone does not indicate whether a difference is beneficial or harmful; that depends on the scientific meaning of the endpoint, and the registry does not define a clinical threshold for interpreting the size of the difference.

The confidence interval gives a range of values compatible with the observed data under the statistical procedure used, while reflecting sampling uncertainty. For the primary comparison, the interval is -5.124 to 48.52 centimeters^2. Because it crosses zero, the data do not distinguish a positive average difference from no average difference or a negative average difference at the conventional two-sided 0.05 significance level. The interval is more informative than a binary significant/not-significant label because it displays both the direction and the range of uncertainty. The confidence level and any details of the registry's original calculation are not reported; the interval displayed with the comparison is the posted one.

The unadjusted p-value is 0.113. In general, a p-value measures how incompatible the observed data are with a null hypothesis, conditional on the assumptions of the test. It does not measure effect size, clinical importance, or the probability that the null hypothesis is true. “Unadjusted” indicates that the value is not corrected for multiplicity in the posted comparison. The statistical test, treatment of any covariates, and the planned significance threshold for the original trial are not reported in the registry record.

A standardized effect-size summary, d, is 0.588, with a pooled standard deviation of 36.92 centimeters^2. Standardization expresses the mean contrast relative to a pooled measure of variability, which can help describe the contrast on a scale that is not tied to the outcome's units. It does not eliminate uncertainty, and it does not by itself say whether a difference matters clinically. The method used to calculate or interpret this statistic is not described in the registry record, so it should be understood as a posted summary rather than evidence of a prespecified analysis.

Randomization supports a causal comparison when allocation is implemented as intended and outcome data are analyzed appropriately. However, the record does not report enough detail to assess the randomization sequence, concealment, masking roles, adherence, or the analysis population. Triple masking is recorded, but the identities of the masked participants or study personnel are not specified. The posted results should therefore be interpreted alongside these reporting gaps rather than assuming that every potential source of bias was controlled.

For the secondary continuous outcome, the registry also reports arm means and standard deviations and an unadjusted mean difference. The same general principles apply: the mean describes the average concentration, the standard deviation describes participant-level variability, and the confidence interval indicates uncertainty in the mean contrast. The number of participants with reported secondary measurements differs from the primary arm counts, but the reasons for that difference are not reported. This limits conclusions about the secondary outcome and makes the missing-data process relevant.

The planning illustrations use a normal approximation, two-sided significance level 0.05, and equal allocation between arms. They set the effect to detect as a stated fraction of the observed effect. These are planning assumptions for hypothetical designs, not evidence of the original trial's design assumptions. The registry does not report its original sample-size justification or whether the trial used interim analyses. No interim-analysis plan is reported, and the absence of registry-listed analyses does not establish what analyses may have been conducted outside the posted record.

Over-dispersion, in a general statistical sense, means that outcome variability is greater than a model assumes. When a model underestimates variability, standard errors can be too small and confidence intervals too narrow. The posted primary analysis is based on continuous arm summaries and does not report a model or a dispersion adjustment, so over-dispersion cannot be assessed from the registry record. More generally, inference depends on assumptions about the outcome distribution and the validity of the variance estimate; the record does not document diagnostic checks or alternative analyses.

11. Confidence Intervals and Precision

The primary mean difference is 21.7 centimeters^2, with a 95% confidence interval from -5.124 to 48.52 centimeters^2. This interval is wide relative to the point estimate and includes zero. It therefore communicates considerable uncertainty about both the size and direction of the average contrast. The data are compatible with a modest negative difference, no difference, or a positive difference extending to a substantially larger measured area in the ketorolac arm.

A confidence interval is not a range containing a fixed percentage of individual participants' measurements. It describes uncertainty about the population-level mean difference under the statistical method and assumptions used. The interval does not mean that every value inside it is equally plausible, and it does not assign a probability to the true effect after the data have been observed. Its practical message is that the registry results do not pin down the average contrast precisely.

The sample sizes contributing to the primary arm summaries are 14 and 16. Individual measurements also show notable spread, with standard deviations of 40.5 and 33.5 centimeters^2. Both the limited number of observations and variability among participants are relevant to the uncertainty in the mean comparison. The record does not report a minimum clinically important difference, so the interval cannot be classified as excluding or including a clinically meaningful effect on the basis of a stated threshold.

The secondary PGE2 comparison also has a broad interval, from -47.63 to 71.63 picograms per milliliter, around a mean difference of 12.0 picograms per milliliter. The secondary measure has fewer ketorolac-arm observations than the primary outcome, and its precision is limited. Taken together, the posted intervals counsel against interpreting point estimates as settled effects. Neither interval alone proves no effect; both leave substantial uncertainty about the underlying average differences.

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 describe hypothetical participants per arm, not total event counts. The trial outcomes are continuous, so the relevant planning quantities are participants per arm. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to a stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the trial's original design assumptions, which are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical design to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column describes the corresponding target for a higher chance of detection. These are design calculations, not probabilities that the trial's result is correct and not measures of the probability that the trial found an effect.

For the primary outcome, the illustration using 100% of the observed effect lists 46 participants per arm for 80% power and 61 participants per arm for 90% power. Planning for 75% of the observed effect lists 81 and 109 participants per arm, respectively; planning for 50% lists 182 and 244 participants per arm. Smaller effects are harder to distinguish from random variation, so detecting them at the same power generally requires more participants. The primary arm counts in the posted results are 14 and 16, which are below those illustrative targets.

A curve representing the planning relationship should be read in the same way: moving toward a smaller effect corresponds to a larger required sample size, with the assumptions held fixed. These figures are not observed power. Observed power is not a useful substitute for examining the effect estimate and its confidence interval; the interval directly displays the uncertainty in the posted comparison. The planning calculations also do not establish why the original trial enrolled its recorded number of participants.

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 = 21.700; pooled standard deviation σ = 36.915.
2. n = 2 × (1.96 + 0.842)² × 36.915² / 21.700² = 45.4, rounded up to 46 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 <- 21.7                      # observed difference in means
sigma <- 36.9154439225644                     # 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(693160)
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 = 46 (80% power), 61 (90% power)
 75% of observed effect: n per arm = 81 (80% power), 109 (90% power)
 50% of observed effect: n per arm = 182 (80% power), 244 (90% power)
power.t.test: 46.4 
Simulated power at n = 46 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. Multiplicity, Missing Data and Analysis Populations

The registry reports one primary outcome and one posted secondary outcome. It does not report a multiplicity strategy, such as a family-wise error adjustment, a false-discovery procedure, or a sequence for testing outcomes. The unadjusted p-values should therefore be interpreted as individual comparisons rather than as results that account for the number of outcomes or any other analyses that may have been considered. This is especially relevant to the secondary result, which is not a confirmatory finding on the basis of the information in the registry.

The record lists no reported analyses. This means the registry does not document a complete analysis plan or a set of sponsor-reported inferential analyses that can be compared with the posted summaries. It does not establish that no analysis was performed. The original statistical analysis plan, covariate adjustments, sensitivity analyses, interim analyses, stopping criteria, and method for handling protocol deviations are not reported in the registry record.

The analysis population is also not reported. The primary summaries include 14 participants in the ketorolac arm and 16 in the placebo arm. For the secondary measure, the posted ketorolac summary includes 11 participants while the placebo summary includes 16. The registry does not explain why the available counts differ across outcomes, whether observations were missing, or how any missing values were handled. It also does not say whether the analysis was intention-to-treat, per-protocol, or based on participants with available outcome measurements.

These reporting gaps matter because missing outcomes can affect both the precision and the interpretation of a comparison. If availability is related to participant characteristics or outcomes, an analysis restricted to observed measurements may not represent the randomized groups in the same way as a complete follow-up analysis. The registry record does not provide enough information to assess that possibility. No assumptions about reasons for missingness or methods of imputation can be inferred from the arm counts alone.

The registry's terminated status does not, by itself, show that the study stopped early for a particular reason, that an interim analysis was conducted, or that multiplicity methods were omitted from the original protocol. Those details are not reported in the registry record. Accordingly, the posted comparisons should be read with attention to both the uncertainty in each estimate and the limited reporting on how the outcomes and analyses were selected.

15. 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 0% reporting threshold.

The registry reports zero participants affected by serious adverse events among 14 participants at risk in the intrathecal ketorolac arm and among 16 at risk in the placebo arm. It also reports zero participants affected by other adverse events among the same respective at-risk counts. These are counts of participants with reported events, not counts of all event episodes, and the record lists no serious adverse event terms.

The death fields are null. A null entry does not document a zero count; deaths are not reported in the registry record. Likewise, the reported zero affected participants should be read as the posted event counts for the listed groups, not as proof that no event occurred outside the definitions or reporting period used.

Safety interpretation is limited by the small enrolled study and the absence of further detail about event definitions, collection procedures, severity grading, follow-up duration, or causal attribution. The registry's adverse-event figures are descriptive and do not establish comparative safety. They should not be generalized beyond the participants and reporting available in this record.

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

The results describe a randomized comparison of intrathecal ketorolac with intrathecal placebo during remifentanil exposure in a capsaicin-induced hypersensitivity model. The primary observed mean area was larger in the ketorolac arm than in the placebo arm, but the confidence interval is broad and includes zero. The posted comparison therefore leaves substantial uncertainty about the average difference. It does not establish a precise direction or size of effect.

The result does not demonstrate equivalence. A non-significant p-value does not show that the groups are the same; an equivalence conclusion would require a prespecified margin and an analysis designed to assess whether the difference lies within that margin. The registry does not report such a margin or equivalence analysis. Likewise, the positive point estimate alone does not establish a clinically important increase, because a threshold for meaningful change is not reported.

The experiment also does not answer whether ketorolac changes pain after surgery, trauma, or nerve injury. The participants were healthy, and the primary outcome came from an induced capsaicin response. This model may be useful for studying a controlled sensory response, but it is not the same as clinical pain in those settings. The posted comparison included remifentanil in both arms, so it does not estimate the effect of remifentanil versus no remifentanil.

The secondary PGE2 result offers a biological measurement but does not establish a mechanism or explain the primary outcome. No mediation analysis or relationship between participant-level PGE2 and hypersensitivity is reported. Both outcome comparisons remain subject to uncertainty, and the secondary result is unadjusted for multiplicity.

Overall, the registry supports a cautious description of what was measured in this small experimental study, not a clinical recommendation or a definitive treatment conclusion. Important protocol and analysis details, including the original sample-size justification, missing-data handling, and analysis populations, are not reported in the registry record. Those limits constrain how far the posted estimates can be carried beyond this experiment.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an observed point estimate and a precise estimate. The primary arm means differ in the posted summaries, yet the confidence interval spans zero and a broad range of possible average differences. Reporting the estimate with its interval makes the uncertainty visible rather than reducing the result to whether a p-value crosses a threshold.

The study also highlights the importance of variability in experimental outcomes. Standard deviations in both arms are substantial, and the primary arm counts are modest. An observed mean contrast can be sensitive to participant-to-participant variation in such a setting. The confidence interval conveys this limitation more directly than a binary conclusion.

A further statistical lesson is that planning depends strongly on the effect size targeted. The registry's planning illustrations show that hypothetical sample requirements increase when the effect to detect is smaller. These calculations are separate from the original trial's design rationale, which is not reported. They should not be mistaken for observed power or for a post hoc validation of the trial's sample size.

Finally, the record demonstrates why transparent reporting of analysis populations, missing data, multiplicity, and prespecified methods matters. Without those details, readers cannot fully assess whether the posted comparisons reflect the planned primary analysis or how robust the conclusions are to alternative decisions. The trial is a useful case for interpreting estimates and uncertainty in a controlled experimental model while recognizing the limits of registry reporting.

18. Limitations

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

The primary endpoint is an induced sensory response in healthy participants rather than pain in a clinical patient population. The capsaicin model was described as milder than pain after surgery or certain nerve injuries. Results from this experimental setting may not translate directly to those conditions. The registry does not report a clinical threshold for a meaningful change in hypersensitivity area, which also limits interpretation of the size of the mean difference.

The primary arm counts are 14 and 16, and the confidence interval is broad. The registry does not report the original sample-size justification, so it is not possible to determine from the record what effect the trial was designed to detect or whether its planned recruitment was met. The current planning illustrations use the observed effect and should not be read as the original design calculation.

Reporting is limited for design and analysis details. Although randomization and triple masking are recorded, the randomization method, allocation concealment, masked roles, and masking procedures are not reported. The analysis population, handling of missing data, covariate adjustment, prespecified multiplicity strategy, and interim analyses are also not reported. The reason for termination is not reported in the registry record.

The secondary PGE2 summary has fewer ketorolac-arm observations than the primary outcome, and the reason is not reported. The record provides no account of missingness or evidence that missing measurements were unrelated to participants' outcomes. Finally, the posted adverse-event counts have limited detail, and the null death fields do not document a zero count. These constraints call for cautious interpretation of both efficacy-related outcomes and safety reporting.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effect of Spinal Ketorolac After Acute Opioid Exposure — NCT00693160.
• Registry record last updated 2018-09-07; status last verified 2018-08.
• Results first posted 2014-04-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00693160 is a randomized, triple-masked, parallel phase 2 study sponsored by Wake Forest University. It enrolled 30 healthy participants and is listed as terminated. The recorded study start was 2007-12 and primary completion was 2010-10. The registry does not report the reason for termination.

The primary comparison was intrathecal ketorolac 2 mg versus intrathecal placebo during remifentanil exposure, using a capsaicin hypersensitivity model. At approximately 24 hours, the posted mean hypersensitivity area was 70.1 centimeters^2 for ketorolac and 48.4 centimeters^2 for placebo. The mean difference was 21.7 centimeters^2, with a 95% confidence interval from -5.124 to 48.52 and an unadjusted p-value of 0.113.

The secondary outcome was cerebrospinal-fluid PGE2 concentration at 2.5 hours. The registry lists no reported analyses. Design rationale, analysis populations, missing-data handling, and multiplicity methods are not reported in the registry record.