Does a Single Intravenous Dose of Ketamine Reduce the Need for Supplemental Opioids in Post-Cesarean Section Patients?: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Does a Single Intravenous Dose of Ketamine Reduce the Need for Supplemental Opioids in Post-Cesarean Section Patients? (NCT00486902), a randomized na study. The primary outcome is Number of Subjects Requiring Supplemental Analgesia in the First 24 Hours Following Cesarean Delivery.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-group trial sponsored by Northwestern University. The registry lists the study as completed, with enrollment of 188. The start is recorded as 2006-07 and primary completion as 2008-10. The phase is listed as NA. The registry record describes two intervention groups: ketamine and placebo.

In the ketamine group, participants received intravenous ketamine 10 mg five minutes after infant delivery. In the placebo group, participants received intravenous saline 20 mL at the same stated time. The trial title and brief summary frame the study around supplemental opioid requirements after cesarean delivery. The primary endpoint was the number of participants requiring supplemental analgesia during the first 24 hours following delivery.

The primary analysis population is described as per protocol. The registry record does not report the detailed eligibility criteria, the specific masking roles, how randomization was generated or concealed, or the original protocol’s planned sample size. It also does not report the original design assumptions or a detailed statistical analysis plan. Those items should not be inferred from the posted outcome counts or the recalculated planning illustrations.

The registry record lists secondary outcomes concerning pain scores at first analgesia request, cumulative hydrocodone/acetaminophen use, postoperative nausea, vomiting and pruritus, and disturbing dreams. Six secondary outcomes are identified as posted. Numerical results for all listed outcomes are not reported in the registry record. The trial’s randomized design supports a group comparison, but interpretation also depends on the analysis population, outcome measurement, and reporting details. Since the primary analysis is identified as per protocol, the available record does not establish that the analysis included every randomized participant or followed an intention-to-treat approach.

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.

Before assignment: 188 subjects were recruited for the study. 5 subjects in the ketamine group and 3 in the saline group were excluded after randomization but before study drug administration.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed per protocol

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Subjects Requiring Supplemental Analgesia in the First 24 Hours Following Cesarean Delivery, measured over 24 hours.

The primary endpoint counts participants who requested oral hydrocodone/acetaminophen for pain that was not controlled by around-the-clock non-steroidal anti-inflammatory drugs during the first 24 hours after cesarean delivery. It is a binary participant-level outcome: each participant either met the stated criterion or did not. The posted value is the number meeting the criterion in each group, rather than a measure of the total amount of opioid consumed.

This endpoint operationalizes the trial’s question about the need for supplemental analgesia. It focuses on breakthrough pain requiring an additional medication request, rather than pain intensity alone. A participant who requested supplemental analgesia contributes to the outcome regardless of the number of requests or the amount taken; those details are not part of the primary measure as described in the registry record.

The endpoint is limited to the stated 24-hour period and medication criteria. It does not, by itself, describe pain scores, timing of the first request, cumulative opioid use, or later recovery. Those topics appear among the listed secondary outcomes, but their numerical results are not reported in the registry record. The primary endpoint should therefore be read as a specific measure of supplemental analgesia use under the study’s stated conditions, not as a comprehensive summary of postoperative pain or recovery.

7. Results Posted in the Registry

• Ketamine: 75.3% (64/85) versus 74.2% (66/89) on control; risk difference 1.1 percentage points (95% CI -11.8 to 14.1), risk ratio 1.02 (0.85–1.21); unadjusted two-proportion z-test p = 0.863.

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.

Postoperative Nausea

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ketamine: 31.8% (27/85) versus 33.7% (30/89) on control; risk difference -1.9 percentage points (95% CI -15.9 to 12.0), risk ratio 0.94 (0.62–1.44); unadjusted two-proportion z-test p = 0.785.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ketamine and the control. The interval gives the range of effects that remain compatible with the data.

Postoperative Vomiting

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ketamine: 15.3% (13/85) versus 14.6% (13/89) on control; risk difference 0.7 percentage points (95% CI -9.9 to 11.3), risk ratio 1.05 (0.52–2.13); unadjusted two-proportion z-test p = 0.899.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ketamine and the control. The interval gives the range of effects that remain compatible with the data.

Postperative Pruritus

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ketamine: 14.1% (12/85) versus 21.3% (19/89) on control; risk difference -7.2 percentage points (95% CI -18.5 to 4.1), risk ratio 0.66 (0.34–1.28); unadjusted two-proportion z-test p = 0.213.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ketamine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of postoperative experience and analgesic use, including pain scores at first analgesia request, cumulative hydrocodone/acetaminophen use, nausea, vomiting, pruritus, and disturbing dreams. The available numerical comparisons show no consistent pattern of large separation across the reported outcomes. Results vary in direction and precision, and the registry record does not report numerical results for every listed secondary outcome.

That broad pattern does not overturn or independently confirm the primary finding. The primary endpoint directly addresses whether a participant requested supplemental analgesia under the specified conditions. Secondary measures can provide additional context, but they address related rather than identical questions. For example, a medication-use measure and a participant’s pain score capture different features of the postoperative course. The registry record does not report enough detail to infer how these outcomes were related at the participant level.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for apparently notable findings. In general, when many statistical tests are considered, the chance of at least one unusual result can increase even if there is no true effect on any outcome. A multiplicity plan can define how to account for that issue, but such a plan is not reported in the registry record. Without it, secondary p-values should be treated as exploratory rather than as independent confirmatory evidence.

The posted secondary comparisons should also be read with attention to their uncertainty intervals and the number of participants analyzed for each outcome. The registry record does not report detailed missing-data methods or whether all outcomes used the same analysis population. For these reasons, the secondary findings are best considered contextual evidence, not a basis for claiming a broad effect across pain, opioid use, or side effects. Their overall pattern is compatible with the primary result’s lack of a clear separation, but it does not establish equivalence among the groups.

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

• Verbal Pain Scores (0 to 10) at First Analgesia Request
• Cumulative Hydrocodone/Acetaminophen for Supplemental Analgesia to Treat Breakthrough Pain
• Postoperative Nausea
• Postoperative Vomiting
• Postperative Pruritus
• Disturbing Dreams

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary outcome, each participant is classified according to whether the event occurred. Here, the event is a request for supplemental analgesia meeting the registry’s definition during the first 24 hours after cesarean delivery. The group counts and the numbers analyzed provide the basis for comparing event frequencies. The primary result is reported as counts, and the recalculation expresses the contrast using risks and relative measures.

What does a risk difference describe?

The risk difference subtracts the event risk in the placebo group from the event risk in the ketamine group. A value of zero corresponds to equal observed risks; a positive value means the event risk is higher in the ketamine group, and a negative value means it is lower. The recalculated risk difference is 0.011. This is an unadjusted comparison based on the posted group counts, not an adjusted model estimate.

In general, the risk difference is useful because it expresses an absolute contrast on the outcome scale. Its meaning depends on the event definition and the population being compared. Relative risk and odds ratio describe the contrast differently. The recalculated relative risk is 1.015 and the recalculated odds ratio is 1.062. In general, a relative risk of one and an odds ratio of one correspond to no relative contrast; values on either side indicate different directions of association. These measures do not remove the uncertainty in the data and should be interpreted together with their intervals.

Why use Fisher’s exact test?

The registry-reported primary analysis names Fisher Exact and reports p = 0.86. In general, Fisher’s exact test evaluates evidence of association in a two-by-two table of event status and group assignment, using the observed margins of that table. It is a method for categorical data and does not require a large-sample approximation for the test calculation. The registry record does not report a more detailed rationale for choosing this test.

The unadjusted recalculation gives p = 0.863. This p-value is based on the posted summary counts, whereas the sponsor-reported analysis is the analysis recorded by the trial. The values are close, but they should not be presented as if they were the same calculation or as independent replications. The sponsor’s own result is the authoritative reported analysis; the recalculation is a descriptive cross-check based on the posted summaries.

How should a p-value be read?

In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and test procedure. It is not the probability that the null hypothesis is true, and it does not show the probability that the result will replicate. A large p-value does not demonstrate equality. A small p-value does not, by itself, show that a difference is important. Interpretation requires the estimated contrast, its uncertainty, the outcome’s clinical context, and the analysis plan.

The registry record identifies the Fisher exact test for the primary comparison, but it does not report whether the test was one- or two-sided. The recalculated sample-size assumptions specify a two-sided significance level of 0.05 for planning illustrations; this is not evidence that the trial’s original analysis plan used that threshold. The original significance threshold and other design assumptions are not reported in the registry record.

What does an interval add?

In general, a confidence interval expresses the range of parameter values reasonably compatible with the data under the interval method and its assumptions. A narrower interval indicates greater precision; a wider interval indicates less precision. An interval that includes zero for a risk difference is compatible with no difference, but it may also include nonzero differences. The recalculated interval for the primary risk difference runs from -0.118 to 0.141, so it spans zero and includes contrasts in both directions.

The registry-reported primary test gives a p-value but no interval estimate in its reported-analysis entry. The interval and effect measures discussed with the primary result are unadjusted recalculations from posted summary statistics. The registry record does not specify the calculation method for those recalculated intervals. The interval should therefore be treated as a precision description of the recalculation rather than a sponsor-reported confidence interval.

For binary outcomes, dispersion is not summarized in the same way as for a continuous measurement such as a mean and standard deviation. The key quantities are the event counts, analyzed group sizes, estimated contrast, and uncertainty interval. The analysis does not adjust for other participant characteristics, and an adjusted model is not reported in the registry record. Any adjusted estimate, alternative model, or subgroup result would require information that is not available in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.011, with an interval from -0.118 to 0.141. Because zero lies within the interval, the posted data are compatible with no difference in event risk. The interval also extends into both negative and positive values, so the results remain compatible with lower or higher event risk in the ketamine group. This uncertainty is central to interpreting the estimate; the point estimate alone does not capture it.

In general, a confidence interval represents uncertainty around an estimate under a specified method and its assumptions. A wide interval indicates that the data do not pin down the effect closely. The primary interval is broad enough to include a range of contrasts, rather than concentrating tightly around zero. Thus, although the point estimate is close to zero, the result should not be read as a precise demonstration of no difference.

The relative measures reinforce the same broad interpretation. The recalculated relative risk is 1.015, with an interval from 0.854 to 1.207, and the recalculated odds ratio is 1.062, with an interval from 0.536 to 2.105. Each interval includes its respective no-association value. Relative measures can sometimes appear different in scale from an absolute risk difference, so the measure should be matched to the question being asked. For the practical question of how event frequency differed between groups, the absolute risk difference is particularly direct.

The registry-reported analysis gives p = 0.86 from Fisher’s exact test. This result is consistent with the recalculated estimate and interval in the limited sense that neither indicates strong evidence of a group difference. It does not establish that effects of all sizes are ruled out. The registry record does not report the original target precision or a prespecified clinically important difference, so the interval cannot be judged against a documented precision target.

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 illustrations express required sample sizes as participants per arm, not as total events. They use the observed effect as a reference and consider planning for 100%, 75%, and 50% of that effect. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These assumptions describe the illustrations, not the trial’s original design, whose sample-size assumptions are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 22,940 participants per arm for 80% power and 30,710 participants per arm for 90% power. Planning for 75% of the observed effect gives 40,934 participants per arm for 80% power and 54,799 participants per arm for 90% power. Planning for 50% of the observed effect gives 92,441 participants per arm for 80% power and 123,752 participants per arm for 90% power.

In plain language, the 80% power column describes the planned per-arm sample size that would give the stated probability of detecting the target effect under the planning assumptions if that effect were present. The 90% column uses a higher target probability of detection and therefore calls for more participants per arm. Smaller target effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants. These figures are planning illustrations, not observed power. They do not show the probability that the trial’s result is correct, and they do not recover the original design rationale.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.742; treatment proportion p₁ = 0.753; average p̄ = 0.747.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6146 = 1.2046.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6145 = 0.5172.
4. n = (1.2046 + 0.5172)² / (0.0114)² = 22,939.6, rounded up to 22,940 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 <- 0.741573033707865                          # control proportion
p1 <- 0.752941176470588                          # 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(486902)
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 = 22,940 (80% power), 30,710 (90% power)
 75% of observed effect: n per arm = 40,934 (80% power), 54,799 (90% power)
 50% of observed effect: n per arm = 92,441 (80% power), 123,752 (90% power)
power.prop.test: 22939.6 
Simulated power at n = 22,940 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a Fisher exact analysis for the primary comparison with p = 0.86. The recalculation from the posted counts gives an unadjusted p-value of 0.863, alongside the recalculated risk difference and its interval. These results are close in numerical terms, but the recalculation is not a replacement for the sponsor’s own analysis. It is a simple check based on the posted summary counts.

The recalculated comparison estimates the risk difference as 0.011, with an interval from -0.118 to 0.141. The sponsor-reported entry gives no estimate or interval, only the test method and p-value. It therefore cannot be treated as a direct comparison of two fully reported effect estimates. The registry record does not describe additional adjustment or analysis details for the sponsor’s result.

There is no flagged discrepancy between the recalculation and the reported analysis. The sponsor’s own reported analysis remains the primary account of the trial’s inferential result, while the recalculation supplies an unadjusted effect-size description from the posted counts. Neither p-value should be interpreted alone, and their closeness does not resolve the uncertainty about the size or direction of a possible effect.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists several secondary outcomes in addition to the primary endpoint, but a plan for controlling multiplicity is not reported in the registry record. Multiplicity matters when many outcomes or comparisons are tested: even if there is no underlying effect, one or more results may appear unusual by chance. In general, prespecifying a primary endpoint and a multiplicity strategy helps distinguish confirmatory tests from exploratory analyses. The primary endpoint is identified, but the full hierarchy or adjustment strategy for the secondary outcomes is not reported in the registry record.

Missing-data handling is also not reported in the registry record. The primary analysis is described as per protocol, but the record does not explain the criteria for inclusion in that population, the number excluded from analysis, or how missing outcome information was treated. It therefore cannot be determined from the registry entry whether missing values were absent, excluded, imputed, or addressed in another way. The record also does not describe sensitivity analyses for missing data.

The analysis population is an important limitation for interpreting a randomized trial. Random assignment creates comparable groups at allocation, while a per-protocol analysis can exclude participants after assignment. In general, post-randomization exclusions may affect the comparability that randomization is intended to support. The registry record does not provide enough detail to assess whether that concern applies or how strongly it might affect the estimate. An intention-to-treat analysis is not reported in the registry record.

Interim analyses, stopping rules, and a detailed statistical analysis plan are not reported in the registry record. The recalculated planning assumptions are not evidence of the trial’s original design or analysis choices. The registry entry therefore supports interpretation of the posted counts and the reported Fisher exact test, but it does not permit a full audit of endpoint selection, multiplicity control, missing-data decisions, or analysis-population rules.

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 0.01% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures show zero affected participants in the ketamine group, with 85 participants at risk, and zero in the placebo group, with 89 participants at risk. The registry record lists no serious adverse event terms. These are counts within the recorded safety groups; they should not be interpreted as proof that serious events cannot occur or that the groups have identical safety profiles.

The separate figures for other adverse events show 30 affected participants among 85 at risk in the ketamine group and 7 among 89 at risk in the placebo group. These counts are distinct from the serious adverse event counts. The registry record does not provide event-level descriptions or further detail in the serious-event summary, and death counts are not reported. The listed counts describe what was recorded; they do not establish causation or explain the nature, severity, or timing of each event.

Safety comparisons are limited by the recorded sample sizes and available detail. A zero count in a group is not evidence of zero underlying risk, particularly when the number observed is limited. Conversely, a difference in counts alone does not establish that the intervention caused the difference. The registry record does not report a detailed safety-analysis method or additional context needed to interpret the other adverse-event counts.

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

The trial addresses a focused question: whether a single intravenous dose of ketamine after infant delivery was associated with fewer requests for supplemental analgesia during the first 24 hours after cesarean delivery. The posted primary counts are similar, and the recalculated risk difference is close to zero. The registry-reported Fisher exact result does not indicate strong statistical evidence of a difference in this endpoint.

That finding is not the same as proof that ketamine and placebo have identical effects. The recalculated interval spans zero and includes contrasts in both directions. It does not rule out every potentially meaningful difference. The registry record does not report a prespecified equivalence margin or a non-inferiority design, so those conclusions cannot be drawn from the nonsignificant test.

The endpoint also has a specific scope. It counts participants requesting a particular supplemental medication under the stated pain-control conditions during a limited period. It does not, by itself, determine pain intensity, overall satisfaction, recovery, later analgesic use, or the balance of benefits and harms. Some related outcomes are listed as secondary, but the registry record does not report numerical results for all of them.

The per-protocol analysis description and missing analysis details further limit interpretation. The registry record does not report how the per-protocol population was defined, how missing outcomes were handled, or whether an intention-to-treat analysis was performed. These details matter when assessing how well the comparison preserves the protection offered by randomization.

The appropriate conclusion is descriptive: the posted primary data show no clear separation in supplemental analgesia requests, while the estimate remains imprecise enough to leave a range of possible differences. The result does not prove benefit, lack of benefit, or equivalence. It should be understood alongside the outcome definition, analysis population, uncertainty, and incomplete reporting of the original design and analysis methods.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect and its uncertainty deserve more attention than a p-value alone. The reported Fisher exact p-value is 0.86, and the unadjusted recalculation is 0.863. Those values do not provide a direct measure of the size of a possible difference. The recalculated risk difference of 0.011 and its interval from -0.118 to 0.141 show both the direction of the point estimate and the range of uncertainty around it.

It also highlights the distinction between failure to detect a difference and evidence of equivalence. The primary counts are similar, but the interval includes contrasts in either direction. A study intended to demonstrate equivalence would require a prespecified margin and an appropriate analysis; the registry record does not report those features. Without them, a nonsignificant result should not be converted into a claim that the groups are the same.

The sample-size illustrations show how the observed effect size influences planning. Under the stated assumptions, targeting a smaller fraction of the observed effect requires a larger per-arm sample. That relationship is general to statistical planning: subtle differences require more information to distinguish them from random variation. These retrospective illustrations do not explain the original trial design or tell us the probability that its result is correct.

Finally, the record demonstrates the importance of transparent reporting. Knowing the analysis population is per protocol is useful, but details about exclusions, missing outcomes, multiplicity, interim analyses, and the original statistical plan are not reported. Those omissions constrain how fully readers can assess bias and precision. Statistical interpretation is strongest when effect estimates, intervals, analysis choices, and missing-data procedures are all described.

19. Limitations

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

The primary outcome is limited to a request for oral hydrocodone/acetaminophen for pain not controlled by scheduled non-steroidal anti-inflammatory drugs during the first 24 hours. It does not summarize all aspects of pain or postoperative recovery. The endpoint’s reliance on a medication request also means that it reflects the study’s stated treatment and decision process, not pain intensity alone.

The primary analysis is described as per protocol, but the registry record does not define that population or explain exclusions. Missing-data handling and an intention-to-treat analysis are not reported in the registry record. These omissions make it difficult to judge the possible effects of post-randomization exclusions or incomplete outcome information.

The record does not report the original sample-size rationale, a prespecified clinically important difference, or a detailed statistical analysis plan. It also does not report a multiplicity strategy for the secondary outcomes or whether interim analyses were conducted. The planning illustrations are based on the observed effects and stated planning assumptions; they cannot substitute for the original design documentation.

The registry-reported primary result gives a test and p-value but no sponsor-reported effect estimate or interval. The effect measures and interval discussed in the recalculation are unadjusted calculations from posted counts. Numerical results for all listed secondary outcomes are not reported in the registry record, and the safety summary lacks event-level detail. Together, these reporting limitations restrict evaluation of precision, analysis choices, outcome coverage, and safety context.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Does a Single Intravenous Dose of Ketamine Reduce the Need for Supplemental Opioids in Post-Cesarean Section Patients? — NCT00486902.
• Registry record last updated 2014-04-14; status last verified 2014-03.
• Results first posted 2011-05-06.
• 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 trial sponsored by Northwestern University. Participants received either intravenous ketamine 10 mg or intravenous saline 20 mL five minutes after infant delivery. The primary endpoint was the number requiring supplemental analgesia during the first 24 hours after cesarean delivery, and the analysis was described as per protocol.

The posted primary counts were 64 of 85 in the ketamine group and 66 of 89 in the placebo group. The registry-reported Fisher exact analysis gives p = 0.86. The unadjusted recalculation gives a risk difference of 0.011, with an interval from -0.118 to 0.141. The estimate is close to zero, but its uncertainty does not establish equivalence or rule out differences in either direction.

The registry record does not report the original sample-size rationale, detailed missing-data methods, multiplicity plan, interim analyses, or full statistical analysis plan. These omissions limit assessment beyond the posted results.