Oral Pregabalin as Preemptive Analgesia in Abdominal Hysterectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral Pregabalin as Preemptive Analgesia in Abdominal Hysterectomy (NCT04495374), a randomized phase 4 study. The primary outcome is Postoperative Pain in Rest Assessed 24 Hours After Abdominal Hysterectomy Surgery Using the Visual Analog Scale (VAS).

2. Clinical Question

The trial’s stated objective was to examine whether preemptive oral pregabalin was associated with postoperative pain and opioid use after abdominal hysterectomy. The primary endpoint narrows that broad objective to a specific outcome: pain at rest at the end of the first postoperative day. Secondary outcomes listed in the record concern opioid rescue use and dizziness, but numeric results are not posted for all of those outcomes.

The question is about the measured outcomes in the groups enrolled in this trial. It is not, by itself, a question about every possible pain outcome, all postoperative recovery, or longer-term effects. The registry record does not report a broader primary outcome covering overall recovery, nor does it provide enough information to characterize how the findings might apply outside the described surgical population.

3. Trial Design

The registry identifies NCT04495374 as a phase 4, randomized, parallel-group trial of oral pregabalin and placebo in abdominal hysterectomy. The recorded enrollment is 58. The listed study start is 2019-09-02, and primary completion is recorded as 2020-09-09. The trial status is terminated. The registry record does not report why it was terminated.

The two groups were placebo and pregabalin 300 mg. The detailed arm descriptions state that the placebo group received two placebo tablets and the pregabalin group received two 150 mg tablets. Both descriptions specify administration 02h before the anesthetic-surgical procedure, with tablets in identical sealed envelopes identified only as medication A or B. The registry’s masking field says triple, while the arm descriptions call the study double blind. The record does not clarify which roles were masked or explain the difference in wording.

The brief summary describes the placebo as being taken one hour before the procedure, whereas the detailed arm descriptions specify 02h before the procedure. This timing inconsistency is not resolved in the registry record. It should not be silently treated as a single, confirmed timing.

The primary endpoint was mean pain at rest measured with the Visual Analog Scale 24 hours after the end of surgery. The record also lists secondary outcomes concerning the number of opioid rescue doses, time to first opioid rescue, and participants with dizziness. Although the registry lists enrollment of 58, the posted primary endpoint group summaries contain 28 participants in the placebo group and 27 in the pregabalin group. The record does not explain the difference between the enrollment figure and those endpoint group counts.

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 Postoperative Pain in Rest Assessed 24 Hours After Abdominal Hysterectomy Surgery Using the Visual Analog Scale (VAS), measured over End of the first postoperative day of abdominal hysterectomy surgery (24 hours after the end of surgery).

The primary endpoint is postoperative pain at rest, assessed at the end of the first postoperative day, 24 hours after the end of abdominal hysterectomy. Pain was measured using a Visual Analog Scale described as a 10 cm line with values from 0 to 10. The scale anchors the low end at absence of pain and the high end at greater pain intensity. The reported endpoint is a group mean, with standard deviation as the measure of spread.

A pain scale provides a structured way to record a participant’s subjective experience. Using a common scale allows the trial to describe and compare the groups at a defined time point. A mean summarizes the central level of reported scores, while the standard deviation indicates how dispersed participants’ scores were around that mean. These summaries do not show the range of individual experiences or whether participants had similar score trajectories over time.

The endpoint is limited to pain at rest at the specified assessment time. It does not directly measure pain during movement, pain at other times, opioid use, or overall recovery. Those broader questions require separate outcome measures. The registry record’s numeric primary result therefore addresses a particular aspect of postoperative pain, rather than every dimension of recovery or analgesia.

7. Results Posted in the Registry

• Group P(1) - Pregabalin 300mg: mean 2.00 versus 5.00 on control; difference -3.00 (95% CI -3.67 to -2.33), standardized effect d = -2.36; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With Dizziness Between the Intervention and Control Groups

• 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:
  • Group P(1) - Pregabalin 300mg: 59.3% (16/27) versus 25.0% (7/28) on control; risk difference 34.3 percentage points (95% CI 9.7 to 58.8), risk ratio 2.37 (1.16–4.84); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group P(1) - Pregabalin 300mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary questions about opioid rescue use and dizziness. The numerical secondary information is incomplete: the registry record does not report numeric results for the number of opioid rescue doses or the time to first opioid rescue. The available secondary evidence therefore cannot establish whether the primary pain contrast was accompanied by a difference in opioid use.

The posted dizziness result points in a different direction from the primary pain result: more participants in the pregabalin group were recorded with dizziness than in the placebo group. This illustrates that secondary outcomes can describe aspects of the experience that are distinct from the primary endpoint. A lower mean pain score does not imply that all other measured outcomes also move in a favorable direction, and the pain measure cannot substitute for a separate assessment of adverse effects or opioid use.

The primary endpoint and the dizziness outcome address different questions and use different kinds of summaries. The primary result compares mean scores on a continuous scale; dizziness is reported as a participant count and compared as a binary outcome. The interpretations should remain outcome-specific rather than combining these measures into a single overall judgment. The registry record does not report a composite measure balancing pain, opioid use, and adverse effects.

Secondary results usually carry less confirmatory weight when their analysis plan and multiplicity handling are not documented. Examining several outcomes can create more opportunities for an apparently notable result, particularly when the outcomes are interpreted separately. The record lists three secondary outcomes but does not provide a multiplicity plan or reported analysis methods. The dizziness finding is therefore descriptive and exploratory in the context of the available registry reporting; the opioid outcomes remain unassessable from posted numeric results.

Taken together, the secondary information does not provide a complete account of the broader analgesia and recovery questions described in the study rationale. It adds a distinct tolerability signal while leaving opioid-rescue outcomes without posted results. It should be considered alongside, but not used to overrule or expand beyond, the specific primary pain comparison.

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

• Number of Doses of Opioids Used as Analgesic Rescue in the Postoperative Period
• Time Required for the Use of the First Dose of Opioid as an Analgesic Rescue in the Postoperative Period
• Number of Participants With Dizziness Between the Intervention and Control Groups

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s pain assessment is represented by a score, and the registry reports a group mean and standard deviation. A natural summary comparison for two independent parallel groups is the difference between their means. The reported direction is pregabalin minus placebo, so a negative estimate indicates a lower mean score in the pregabalin group. This sign convention matters: reversing the subtraction order would reverse the sign without changing the underlying separation.

What does the mean difference describe?

The mean difference places the contrast in the original VAS units rather than in a standardized scale. This makes the estimate directly interpretable as a difference in average points on the pain scale. It does not mean that every participant had a score equal to the group mean, or that every participant’s pain changed by the amount of the group contrast. A group mean is a summary across participants; individual observations may be more or less dispersed, as the standard deviations indicate.

The simple calculation uses the posted group means, group counts, and standard deviations. The registry record does not report that the sponsor used this exact calculation as its primary analysis. No reported primary analysis is listed, so there is no posted sponsor analysis to compare with the recalculation. The recalculated result should be understood as a transparent unadjusted comparison of the summary statistics, with no adjustment for baseline characteristics or other factors.

What does the confidence interval add?

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. It conveys uncertainty in the estimated group difference, rather than merely marking whether a threshold for statistical significance was crossed. In this result, the interval for the mean difference is -3.669 to -2.331. The interval does not include zero, the value corresponding to no mean difference. Its width reflects the estimated sampling uncertainty under the unadjusted calculation; it does not include all possible sources of uncertainty, such as missing data, measurement limitations, or bias in trial conduct.

The reported p-value is unadjusted. A p-value is a measure of how compatible the data are with a specified null model, given the assumptions of the test. It is not a measure of effect size, clinical importance, or the probability that the null hypothesis is true. It should be interpreted alongside the estimated mean difference and confidence interval, not as a stand-alone verdict.

Why can the standard deviation matter?

The standard deviation describes how variable participant scores are within a group. When participant outcomes vary substantially, the group mean is estimated less precisely for a given number of participants than it would be with less variability. This is one reason both the group sizes and the outcome spread matter when estimating a difference. The posted summaries include a standard deviation for each group, and the recalculation uses those summaries rather than individual participant-level observations.

Some statistical models require attention to distributional assumptions. For a continuous outcome, an analysis based on means commonly relies on the estimate behaving adequately under the model used for inference. The registry record does not report diagnostic checks, a distributional model, or any alternative analysis. It is therefore not possible to assess from the record whether the original investigators evaluated these assumptions or used a different method.

What does an unadjusted analysis leave out?

An unadjusted comparison contrasts the observed groups without accounting for other measured characteristics. Random allocation is intended to make groups comparable on average, but the record does not report baseline characteristics or an adjusted model for this endpoint. Without those details, the reader cannot assess the balance of measured prognostic factors or determine whether an adjusted estimate would differ. The posted group summaries also do not permit assessment of participant-level relationships or tailored analyses.

The primary result is based on outcome counts of 28 in the placebo group and 27 in the pregabalin group. The registry record gives overall enrollment as 58 but does not explain how the endpoint counts relate to that total. It does not report whether participants were analyzed as randomized, whether any observations were missing, or how missing endpoint values were handled. These omissions matter because the assumptions behind a group comparison depend in part on which participants contribute data and why.

What is the role of the secondary analyses?

The record lists secondary outcomes, but numeric results are posted only for dizziness among the listed secondary results. It does not report analyses for the opioid rescue outcomes. When many outcomes are considered, the chance of finding a nominally unusual result can increase if the analyses are treated as independent opportunities for significance. A multiplicity plan can specify how such comparisons are interpreted or adjusted. No such plan is reported in the registry record, so an unadjusted secondary p-value should not be given the same confirmatory weight as a prespecified primary endpoint result.

The record’s analysis count is zero, and no reported analyses are listed for the posted secondary result. This does not mean that no statistical work was done; it means the registry record does not document reported analysis methods. The available statistical comparisons should consequently be read as limited summaries of the posted outcomes, with important details of the original analysis plan and execution not reported.

11. Confidence Intervals and Precision

The primary mean difference is -3.0 VAS points, with a 95% confidence interval from -3.669 to -2.331. The interval is the main direct indication of precision in the posted primary comparison. It lies entirely on the negative side of zero, which is consistent with a lower average score in the pregabalin group under the stated subtraction order. The interval is not a range containing a known fixed proportion of individual participant scores; it describes uncertainty in the estimated group difference.

The confidence interval is fairly concentrated around the point estimate relative to the full 0-to-10 scale, but that does not capture every form of uncertainty. It relies on the unadjusted method and available summary data. It cannot account for possible bias, incomplete outcome reporting, unknown missing-data handling, or unresolved details of trial conduct. The registry record does not report whether the primary comparison was adjusted or whether other analyses produced different estimates.

Precision should also be distinguished from importance. A confidence interval can indicate that the estimated mean difference is not especially uncertain under a model, while the record still lacks a reported threshold for a clinically important difference. Statistical precision alone does not establish how meaningful the difference is to patients, nor does it describe variability in individual responses. The standard deviations show that participant scores varied within both groups, but the registry record does not provide individual data or a fuller account of the score distributions.

The interval does not address external validity. It summarizes the estimate for the participants represented in the posted endpoint counts and depends on the calculation’s assumptions. The record does not report why enrollment and endpoint counts differ, or whether all randomized participants were included. Those uncertainties are separate from the numerical width of the confidence interval and should remain part of the interpretation.

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 displayed planning figures are participants per arm, not total participants. They are illustrations based on the observed effect, not the trial’s original design calculation. The registry record does not report the trial’s own sample-size justification or original design assumptions.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect. The rows therefore illustrate planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The corresponding figures describe participants per arm for 80% power and participants per arm for 90% power.

Power is the probability, under the assumed effect and planning model, of detecting a difference using the specified significance criterion. The 80% and 90% columns represent different target probabilities in that planning exercise; the higher target generally requires more participants under otherwise similar assumptions. The figures are not estimates of what power the completed trial had. They are planning illustrations, not observed power.

The pattern across the rows demonstrates why the assumed effect matters: planning for smaller effects requires more participants. A design based on a large anticipated effect can produce a smaller planning requirement than one intended to detect a more modest effect. Because the observed effect in a small trial can be uncertain, these calculations should not be treated as a validated recommendation for a future study. The registry record does not report the investigators’ original assumptions, and the planning illustrations do not fill that gap.

For the primary continuous outcome, the listed per-arm figures are 3 and 4 for planning at 100% of the observed effect, 5 and 7 at 75%, and 12 and 16 at 50%, for the 80% and 90% targets respectively. The secondary dizziness planning illustration uses its own observed effect and produces different figures. These values are theoretical planning outputs under the stated assumptions, not evidence about the design or conduct of the terminated trial.

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 = -3.000; pooled standard deviation σ = 1.269.
2. n = 2 × (1.96 + 0.842)² × 1.269² / -3.000² = 2.8, rounded up to 3 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 <- -3                      # observed difference in means
sigma <- 1.26863319705865                     # 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(4495374)
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 = 3 (80% power), 4 (90% power)
 75% of observed effect: n per arm = 5 (80% power), 7 (90% power)
 50% of observed effect: n per arm = 12 (80% power), 16 (90% power)
power.t.test: 4 
Simulated power at n = 3 per arm: 0.591 (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 record does not report a statistical analysis plan, a multiplicity strategy, or reported analyses for the primary and secondary outcomes. It lists one primary endpoint and several secondary outcomes, but does not explain whether any secondary outcomes were intended to be confirmatory, how their tests would be interpreted together, or whether adjustments for multiple comparisons were planned.

Multiplicity matters when a trial examines more than one outcome or makes several statistical comparisons. If each result is treated as an independent opportunity to find evidence against a null hypothesis, the chance of at least one apparently unusual result can increase. A prespecified hierarchy, adjustment, or other strategy can help distinguish primary confirmatory testing from secondary exploration. No such strategy is reported in the registry record, so the unadjusted secondary p-value should be interpreted cautiously.

The registry’s posted primary comparison is an unadjusted recalculation from group summary statistics. The record does not describe covariate adjustment, the statistical model used by the investigators, or whether an intention-to-treat or other analysis population was specified. It does not state how protocol deviations, withdrawals, or missing outcomes were handled. The endpoint summaries include 28 participants in the placebo group and 27 in the pregabalin group, while the recorded enrollment is 58; the reason for this difference is not reported in the registry record.

Missing-data handling can affect both the estimate and its uncertainty, depending on how much information is absent and why. The registry record does not report missingness by group, reasons for missing data, imputation, or sensitivity analyses. It is therefore not possible to determine whether the posted summaries represent all randomized participants or how any unavailable outcomes were treated.

These gaps do not prove that particular methods were or were not used. They mean that the registry record does not document the choices needed to assess the analysis fully. Interpretation should distinguish the posted numerical summaries from unreported protocol and analysis details, rather than assuming a specific plan.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the placebo group among 28 participants at risk and zero in the pregabalin group among 27 participants at risk. It also reports zero deaths in both groups. These are the serious-event figures recorded for the posted safety information.

A count of zero in the observed trial record means that no serious adverse events were recorded in the listed groups during the reporting period. It does not establish that a serious event could never occur, or that the groups have identical safety profiles. The number of participants and the duration and completeness of safety follow-up matter when interpreting a zero count; the registry record does not give enough detail to characterize follow-up comprehensively.

The registry also records other adverse events in both groups, but these are distinct from serious adverse events. The serious-event figures should not be combined with the other-event counts or interpreted as a complete safety assessment. The record does not report detailed event terms for serious adverse events because none are listed, and it does not provide a full narrative account of safety monitoring.

These figures describe what was recorded in this trial, not a general guarantee of safety. They should be read with the limited group counts, the terminated status, and the absence of fuller reporting on follow-up and analysis.

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

The posted primary data support a specific statistical description: at the 24-hour assessment, the pregabalin group had a lower mean pain score at rest than the placebo group. The unadjusted recalculated difference is -3.0 points, with a confidence interval from -3.669 to -2.331 and an unadjusted p-value of <0.001. These results describe the measured endpoint in the participants represented by the posted group summaries.

They do not establish that every participant experienced less pain, that pain was lower at all times or during activity, or that opioid use was reduced. The listed opioid rescue outcomes have no numeric results in the registry record. The result also does not establish an overall recovery benefit, since the record does not report a single comprehensive recovery outcome for this comparison.

Statistical evidence and clinical importance are related but different. The record does not report a threshold for a clinically important difference on the VAS. The estimate and its interval describe the size and precision of the group contrast under an unadjusted calculation; they do not by themselves determine how important that contrast is to patients or clinicians. Nor do they show how much participants’ responses varied beyond the group-level standard deviations.

The result should not be generalized automatically beyond patients undergoing abdominal hysterectomy for benign pathologies as described in the record. The trial was terminated, and the reason is not reported. The registry does not explain the difference between its enrollment figure and primary endpoint counts, or document the handling of missing outcomes and the planned analysis population. These gaps leave uncertainty around completeness and conduct that cannot be resolved from the posted summaries.

The secondary findings do not fill those gaps. Dizziness was reported more often in the pregabalin group, while numeric findings for the opioid rescue outcomes are not reported. With no documented multiplicity plan or analysis methods, those secondary results provide limited support for broader conclusions. The appropriate reading is a result about a defined pain score and time point, accompanied by incomplete secondary and methodological reporting—not a definitive account of all benefits, harms, or recovery effects.

17. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation requires more than reading a p-value. The primary result includes a group difference and confidence interval, which communicate both the direction and estimated precision of the pain-score contrast. Interpreting those statistics also requires attention to the measurement scale, the unadjusted nature of the recalculation, and what the interval does not capture.

It also shows the importance of separating a primary endpoint from secondary outcomes. Pain at rest, opioid rescue use, and dizziness are related to postoperative care but are not interchangeable measures. The primary result cannot answer whether opioid use differed when those numeric results are absent, and a secondary adverse-event comparison should not be folded into the pain estimate. A prespecified approach to multiple outcomes would help clarify the evidential role of each result, but such a plan is not reported in the registry record.

Trial records are most informative when they connect enrollment, randomized groups, analyzed participants, and statistical methods. Here, the enrollment figure and primary endpoint group counts do not match, and the record does not explain why. The masking label and arm descriptions also use different terms, and the timing descriptions are inconsistent. These discrepancies do not establish that the trial was conducted incorrectly, but they limit the reader’s ability to reconstruct its conduct.

Finally, planning illustrations based on an observed effect should not be confused with the trial’s own sample-size rationale or with power observed after completion. The record does not report the original design assumptions. Clear distinction between planning calculations, posted summaries, and documented trial analyses is central to responsible interpretation.

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 registry record leaves several trial-specific uncertainties. The study is marked terminated, but the reason for termination is not reported. Enrollment is recorded as 58, while the primary outcome summaries include 28 participants in the placebo group and 27 in the pregabalin group. The registry record does not explain the difference, identify any missing outcome data, or describe whether participants were excluded from the analysis.

There are inconsistencies in descriptions of trial conduct. The masking field says triple, but the arm descriptions call the study double blind. The brief summary describes dosing one hour before the procedure, while the detailed arm descriptions specify 02h beforehand. The record does not resolve either inconsistency, so a reader cannot identify one definitive masking description or administration time from the registry record alone.

The record does not report the original sample-size justification, the statistical analysis plan, the analysis population, covariate adjustment, missing-data methods, or sensitivity analyses. It does not provide baseline characteristics or individual participant data. Consequently, it is not possible to assess group balance, inspect the outcome distributions, or determine whether other analysis choices would produce different estimates.

The primary endpoint is limited to pain at rest at 24 hours. The opioid rescue outcomes are listed, but numeric results are not reported in the registry record. The available secondary result on dizziness does not substitute for opioid-use results or a comprehensive recovery measure. The record also does not specify a clinically important threshold for the pain scale or a multiplicity strategy for the secondary outcomes.

These limitations concern what can be established from the registry record. They do not prove that unreported procedures were absent; they mean that the record does not document them sufficiently for independent assessment.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Oral Pregabalin as Preemptive Analgesia in Abdominal Hysterectomy — NCT04495374.
• Registry record last updated 2021-03-04; status last verified 2021-02.
• Results first posted 2021-03-04.
• 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

NCT04495374 is a phase 4, randomized, parallel-group trial of pregabalin 300 mg versus placebo before abdominal hysterectomy. The registry records enrollment of 58 and trial status as terminated. The primary endpoint is mean pain at rest on the VAS at 24 hours after surgery.

The posted primary summaries show means of 5.0 in the placebo group and 2.0 in the pregabalin group. The unadjusted recalculated mean difference is -3.0, with a 95% confidence interval from -3.669 to -2.331 and p < 0.001. The registry lists secondary outcomes for opioid rescue and dizziness; numeric opioid results are not reported, while a dizziness result is posted.

The record does not report the trial’s original sample-size rationale, detailed analysis plan, missing-data handling, or reason for termination. It also leaves unresolved inconsistencies in timing and masking descriptions, and does not explain the difference between enrollment and primary endpoint group counts.