Surgical Pain After Inguinal Hernia Repair (SPAIHR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Surgical Pain After Inguinal Hernia Repair (SPAIHR) (NCT00551135), a randomized phase 3 study. The primary outcome is Modified Brief Pain Inventory-Short Form (mBPI-sf): Worst Pain 24 Hours Post Surgery.

2. Clinical Question

The study’s stated purpose was to test whether pregabalin added to standard care would decrease acute postoperative pain after inguinal hernia repair. The endpoint is a patient-reported rating, rather than a direct measure of tissue injury or a clinician’s assessment. The registry reports results for the modified intent-to-treat population, not simply everyone enrolled. The population restrictions and the site exclusion therefore matter when interpreting how widely the posted result applies. The original protocol’s detailed eligibility criteria and the reason for the site exclusion are not reported in the registry record.

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, parallel-group, dose-ranging study. The official title identifies it as multicenter. Participants were assigned to pregabalin 50 mg, pregabalin 150 mg, pregabalin 300 mg, or placebo. The study summary says pregabalin dosing started preoperatively and continued for 1 week after surgery, as an addition to standard care. The registry lists an enrollment of 425 and marks the study as completed.

The registry gives a start date of 2008-01 and a primary completion date of 2009-06. Those dates describe the trial’s recorded timeline; they do not, by themselves, identify when the results were analyzed or posted. Detailed descriptions of the dose schedules, the standard-care regimen, allocation concealment, and the conduct of masking are not reported in the registry record. The arm-description entries are blank, so additional arm-level procedures cannot be established from those entries.

The primary endpoint analysis used a modified intent-to-treat population. It included participants who took study medication at both specified preoperative times, had no complications during herniorrhaphy, and had a post-surgery primary efficacy measurement. The registry says one site’s data were excluded, but the stated reason ends after “Good Clinical”; the rest of that explanation is not reported in the registry record. These restrictions distinguish the primary analysis population from the full enrollment and should be kept in view when reading the endpoint estimates.

The record lists 27 outcome measures and 480 analyses. It does not report the original sample-size justification, the planned primary statistical model in sufficient detail, any interim-analysis plan, or the intended approach to multiplicity. The available record therefore describes key design features and posted results but does not establish every decision that shaped the trial’s conduct or analysis.

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:

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat Population (MITT): all subjects included in intent-to-treat population who took study medication 12 and 2 hours prior to surgery, had no complications during herniorrhaphy, and had the post-surgery primary efficacy measurement. Data from 1 site excluded due to Good Clinical Practices (GCP) deviations.

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 Modified Brief Pain Inventory-Short Form (mBPI-sf): Worst Pain 24 Hours Post Surgery, measured over 24 hours post surgery.

The primary endpoint was worst pain during the 24 hours after surgery, measured with the modified Brief Pain Inventory-Short Form (mBPI-sf). The registry describes the instrument as a self-administered 11-point Likert rating scale. The worst-pain item ranges from 0, meaning no pain, to 10, meaning worst imaginable pain. A lower score represents a lower reported pain rating on this scale.

Pain intensity is a patient-reported experience, so a direct report can capture the participant’s perception rather than relying only on an external observation. Asking about the worst pain in a defined period focuses on the most intense pain recalled during that period; it does not describe every moment of pain or pain’s effect on function. The specified timeframe was 24 hours post surgery.

The registry reports least-squares means and standard errors for the modified intent-to-treat population. A least-squares mean is a model-based group estimate, and its interpretation depends on the analysis model. The registry does not give the model details needed to assess adjustment variables or other modeling choices. It also does not report a threshold for a clinically important difference on this endpoint. Thus, the score’s scale and direction are clear, but the posted values alone do not establish how meaningful a particular difference would be to participants.

7. Results Posted in the Registry

• Pregabalin 50 mg: mean 5.20 versus 5.40 on control; difference -0.20 (95% CI -0.87 to 0.47), standardized effect d = -0.08; z-test p = 0.556.
• Pregabalin 150 mg: mean 5.40 versus 5.40 on control; difference 0.00 (95% CI -0.68 to 0.68), standardized effect d = 0.00; z-test p = 1.000.
• Pregabalin 300 mg: mean 4.70 versus 5.40 on control; difference -0.70 (95% CI -1.37 to -0.03), standardized effect d = -0.29; z-test p = 0.039.

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.

Numeric Rating Scale (NRS): Current Pain at Rest - Area Under the Curve (AUC)

• 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 errors.
• Result:
  • Pregabalin 50 mg: mean 133.80 versus 135.10 on control; difference -1.30 (95% CI -23.11 to 20.51), standardized effect d = -0.02; z-test p = 0.907.
  • Pregabalin 150 mg: mean 141.30 versus 135.10 on control; difference 6.20 (95% CI -15.77 to 28.17), standardized effect d = 0.08; z-test p = 0.580.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 50 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 150 mg and the control. The interval gives the range of effects that remain compatible with the data.

Amount of Non-opioid Rescue Medication (Naproxen and Antiemetic Medications) Used During the Study

• 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 errors.
• Result:
  • Pregabalin 50 mg: mean 3,939 versus 3,770 on control; difference 168.74 (95% CI -258.74 to 596.22), standardized effect d = 0.11; z-test p = 0.439.
  • Pregabalin 150 mg: mean 3,931 versus 3,770 on control; difference 160.50 (95% CI -267.23 to 588.23), standardized effect d = 0.10; z-test p = 0.462.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 50 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 150 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures of pain at rest and with movement, pain averages and area-under-the-curve summaries, time to first rescue medication, and medication use. It reports 26 secondary outcomes, while the record lists 27 outcome measures overall. The posted results cover a broad set of symptoms and treatment-related measures rather than a single additional confirmation of the primary endpoint.

Across the secondary comparisons for which recalculations are available, the estimates do not form a uniformly favorable pattern for pregabalin. The directions vary by comparison, and the recalculated confidence intervals include no difference for the listed contrasts. The registry’s own ANOVA p-values are also reported for some of these comparisons. These high-level features can be read alongside the primary endpoint, but they do not erase the primary analysis discrepancy or independently establish a consistent treatment effect. The displayed secondary comparisons do not include every dose for every endpoint.

Secondary outcomes can provide context about pain over time, pain in different circumstances, and use of rescue medication. They are not automatically confirmatory simply because they are clinically relevant. When many endpoints, doses, timepoints, and analyses are considered, unadjusted results carry less weight: some results may appear notable by chance, and selective emphasis can distort the overall picture. The registry lists 480 analyses but does not report how multiplicity was managed, which analyses were pre-specified, or whether a hierarchy governed interpretation.

For these reasons, the secondary findings are best treated as exploratory context unless the trial’s analysis plan establishes otherwise. That plan is not reported in the registry record. They should be considered together with the primary endpoint, the sponsor-reported analyses, uncertainty in the estimates, and the limitations of the available summary reporting, rather than as repeated independent proof of the primary result.

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

• Numeric Rating Scale (NRS): Current Pain With Movement - Sitting
• Numeric Rating Scale (NRS): Current Pain With Movement - Walking
• Numeric Rating Scale (NRS): Current Pain With Movement - Coughing
• Numeric Rating Scale (NRS): Current Pain With Movement - Area Under the Curve (AUC) for Sitting, Walking, and Coughing
• Numerical Rating Scale (NRS): Current Pain at Rest
• Numeric Rating Scale (NRS): Current Pain at Rest - Area Under the Curve (AUC)
• Numeric Rating Scale (NRS): Average Pain
• Time From End of Surgery to First Rescue Medication

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group average. It is often used when an analysis model accounts for factors beyond the raw group mean. The registry identifies the primary endpoint estimates as least-squares means, but does not describe the model terms or adjustment variables. That omission limits independent assessment of exactly what the estimates represent. A standard error describes the estimated uncertainty of a model-based mean; it is not the spread of individual participants’ pain ratings.

What is a mean difference?

A mean difference compares the estimated average in one group with the estimated average in another. In the recalculations, the comparison is pregabalin minus placebo. A negative estimate therefore indicates a lower estimated score in the pregabalin group; a positive estimate indicates a higher estimated score. These are unadjusted calculations based on the posted group summaries, not an alternative fitted model using participant-level records. The distinction matters because the registry’s least-squares means may reflect modeling choices that the summary statistics do not capture.

How should a confidence interval be read?

A confidence interval expresses uncertainty around an estimated difference under the assumptions used to construct it. It gives a range of values compatible with the data and method; it is not a guarantee that the true difference lies in the interval. A wide interval indicates that the estimate is imprecise, while a narrow interval indicates greater precision. For a difference, an interval that includes zero is compatible with no group difference as well as with differences in either direction. The recalculated intervals are not registry-reported intervals: they are derived from posted summary statistics and should be read as such.

What does a p-value add?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It does not give the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A p-value also does not resolve uncertainty about which analysis was intended. In this trial, the registry reports multiple p-values for the 300 mg versus placebo group pair, and the recalculated p-values differ from the sponsor’s reported values. That disagreement makes the sponsor’s stated analysis especially important to distinguish from the simple recalculations.

Why can recalculations differ from a trial analysis?

Recalculation from summaries necessarily uses less information than an analysis of participant-level data. The posted group results include standard errors, not raw observations or full model details. The recalculated pooled standard deviations are marked as approximate, and the recalculated comparisons are unadjusted. A sponsor analysis may use a different model, population handling, variance estimate, or other analysis choices. The registry record does not provide enough detail to determine which choices explain the observed discrepancies. Consequently, these calculations are best treated as transparent checks based on the posted summaries, not a reconstruction of the sponsor’s analysis.

Why do multiple outcomes complicate interpretation?

Testing many doses, endpoints, timepoints, and analysis variants creates multiple opportunities for apparently notable results. If each comparison is considered on its own without accounting for the full family of tests, the apparent evidence can be overstated. This is the general statistical reason that unadjusted secondary results should be treated cautiously. The record lists 27 outcome measures and 480 analyses, but does not report a multiplicity adjustment strategy or identify a pre-specified hierarchy that would show how the tests were to be interpreted together. The number of posted analyses does not itself reveal how many were planned, nor does it establish which results were confirmatory.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variation is greater than a model assumes. If a model understates variability, standard errors can be too small, confidence intervals too narrow, and p-values too favorable. Appropriate modeling can address over-dispersion when the outcome and design warrant it. The registry does not report a diagnostic assessment or an over-dispersion adjustment for this endpoint, so no conclusion about whether that issue arose in this trial can be drawn.

In this trial, the primary endpoint is continuous and the posted summaries are least-squares means with standard errors. That makes mean-based comparisons relevant, but it does not eliminate the need for the underlying model details. The study’s randomized, double-blind, parallel design supports comparison of assigned groups in principle; interpretation of the actual estimates still depends on the defined analysis population, the model, missing-data handling, and multiplicity decisions. Several of those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary endpoint estimates are accompanied by standard errors, and the recalculations give confidence intervals for the differences between each pregabalin dose and placebo. The intervals are useful for judging precision: they show a range of effect sizes compatible with the summary data and calculation method, rather than only a single point estimate. An interval that spans zero leaves the direction of the difference uncertain under that method. An interval that does not span zero can still be affected by analysis choices and multiplicity.

For the 50 mg comparison, the recalculated mean difference is -0.2, with a confidence interval from -0.865 to 0.465. For the 150 mg comparison, the difference is 0.0, with a confidence interval from -0.679 to 0.679. For the 300 mg comparison, it is -0.7, with a confidence interval from -1.365 to -0.035. These are recalculated intervals from posted summary statistics, not confidence intervals reported by the sponsor. The calculations use approximate standard deviations inferred from the standard errors and are unadjusted.

The intervals should not be read in isolation from the registry’s own analyses. The sponsor’s reported p-values differ from the recalculated p-values, and the registry lists two p-values for the 300 mg versus placebo pair without explaining the distinction. The sponsor’s own analysis takes precedence. The record does not report a clinically important difference threshold, so the intervals cannot be classified as ruling out differences that matter to patients. More precise estimates would narrow uncertainty, but precision alone would not establish clinical importance or resolve the analysis discrepancy.

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 are illustrations based on the observed effect, not the trial’s original sample-size design. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers detecting the stated fraction of the observed effect. The record does not report the trial’s own original design assumptions or sample-size justification.

For these continuous-outcome comparisons, the displayed figures are participants per arm. They are not total participants across both groups. The two power columns describe different planning targets: 80% power means a design with an 80% chance of detecting the specified effect under the assumptions if that effect is real; 90% power uses a higher chance of detection under those same assumptions. Power is a property of a planned study under stated assumptions, not a guarantee that a result will be statistically significant.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the planning requirement changes when the target effect changes. Smaller effects need more participants to detect because they are harder to distinguish from random variation. This relationship is especially important when an observed effect is modest or uncertain: planning around a single observed estimate can be fragile, and a smaller target effect can imply substantially larger recruitment needs.

These figures are not observed power for the completed trial. They are planning illustrations generated from the observed summary effect and the stated assumptions. They do not show the probability that the completed trial’s finding is true, and they do not establish whether the original study was adequately planned. The registry’s original rationale and assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.200; pooled standard deviation σ = 2.418.
2. n = 2 × (1.96 + 0.842)² × 2.418² / -0.200² = 2,294.4, rounded up to 2,295 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.2                      # observed difference in means
sigma <- 2.4179626307249                     # 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(551135)
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 = 2,295 (80% power), 3,072 (90% power)
 75% of observed effect: n per arm = 4,080 (80% power), 5,461 (90% power)
 50% of observed effect: n per arm = 9,178 (80% power), 12,287 (90% power)
power.t.test: 2295.4 
Simulated power at n = 2,295 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The recalculated primary comparisons are simple, unadjusted comparisons derived from the posted group means and standard errors. The registry’s own analyses are listed as ANOVA p-values. These are not interchangeable displays of one necessarily identical calculation: model specification, variance estimation, analysis population, and other choices can affect results. Those details are not reported sufficiently to reproduce the sponsor’s analyses from the registry record.

For pregabalin 50 mg versus placebo, the recalculated p-value is 0.556, while the registry lists 0.693. For pregabalin 150 mg versus placebo, the recalculated p-value is 1.0, while the registry lists 0.800 twice. For the 300 mg versus placebo comparison, the recalculated p-value is 0.039, while the registry lists both 0.067 and 0.033. No explanation is reported for the duplicate p-values for the 150 mg or 300 mg group pairs.

The discrepancy flag applies to these comparisons. The sponsor’s own analysis takes precedence; the unadjusted recalculations should not be presented as corrections or used to choose among the sponsor’s reported p-values. The registry does not explain the discrepancies, provide enough analysis detail to reproduce the results, or identify which of the two p-values for 300 mg is the intended primary result. The appropriate reading is to report the conflict plainly and avoid claiming that the recalculation settles it.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, dose, timepoint, or analysis. Repeated testing increases the chance that at least one result will look unusual even if there is no underlying effect. General statistical approaches can control that risk by adjusting significance thresholds, defining a testing hierarchy, or specifying a limited set of confirmatory comparisons in advance. The registry record does not report whether any such approach was used for this trial.

The record lists 27 outcome measures and 480 analyses. Those counts indicate a substantial range of reported analyses, but they do not reveal which analyses were planned in advance, which were exploratory, or how the results were selected for reporting. It is not reported in the registry record whether the primary comparisons were adjusted for the number of dose comparisons, how secondary outcomes were handled, or whether the two listed p-values for the 300 mg versus placebo comparison reflect different analysis conventions.

Missing-data handling is also not reported in sufficient detail. The primary population requires a post-surgery primary efficacy measurement, which means participants without that measurement do not meet the stated primary analysis definition. The registry does not describe imputation, sensitivity analyses, reasons for missing measurements, or how missingness was assessed. It also does not provide the full participant flow needed to evaluate the consequences of those exclusions.

The primary analysis population was narrower than the randomized population: participants had to take study medication at both specified preoperative times, have no herniorrhaphy complications, and have the primary measurement. In addition, the registry says data from one site were excluded, with the explanation truncated after “Good Clinical.” The full reason and its consequences are not reported in the registry record. These population choices may affect how the estimates generalize and how potential bias should be assessed.

The registry also does not report the original protocol’s detailed statistical plan, the planned interim analyses, or the original sample-size justification. Without those details, it is not possible to determine from the posted record which analysis was intended as definitive or whether the observed differences followed the pre-specified plan.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: amnesia (0.9%), abdominal pain (0.9%), gastric ulcer haemorrhage (0.9%), vomiting (0.9%), pyrexia (0.9%).

The registry reports serious adverse events and other adverse events by safety group. For serious adverse events, the at-risk and affected counts were 108 and 3 for pregabalin 50 mg, 106 and 1 for pregabalin 150 mg, 103 and 0 for pregabalin 300 mg, and 108 and 3 for placebo. For other adverse events, the respective at-risk and affected counts were 108 and 46, 106 and 44, 103 and 56, and 108 and 45. These are registry counts; no group totals or additional rates are calculated.

The registry lists Amnesia, Abdominal pain, Gastric ulcer haemorrhage, Vomiting, Pyrexia, and Muscular weakness among the top serious adverse event terms, each reported as 0.9%. The registry record does not report death counts. Counts of affected participants do not indicate event severity beyond the serious/non-serious classification, duration, causality assessment, or whether multiple events occurred in one participant. The listed terms should not be treated as a complete account of all safety events.

Safety comparisons require context, including the event definitions, follow-up completeness, and how events were collected and assessed. Those details are not reported in the registry record. The posted figures describe reported events in the study groups; they do not by themselves establish comparative safety or justify a treatment decision.

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

The posted primary endpoint describes participants’ reported worst pain during the 24 hours after surgery. The group estimates range from 4.7 to 5.4 on the mBPI-sf item’s scale from 0 to 10. The recalculated comparison for the 300 mg group is lower than placebo, while the recalculated comparisons for the 50 mg and 150 mg groups do not show a clear direction. Those calculations are unadjusted and conflict with the sponsor’s reported analyses. The sponsor’s own analysis takes precedence.

The result does not establish that pregabalin works or does not work. The record contains uncertainty about the primary comparison because the sponsor-reported p-values and recalculated results differ, and two sponsor p-values are listed for the 300 mg versus placebo pair. The record does not explain the discrepancy. It also does not report a clinically important difference threshold, so the statistical estimates cannot be translated into a judgment about whether any score difference would matter to participants.

The study examined pregabalin added to standard care, with preoperative dosing continuing for 1 week after surgery. Its randomized, double-blind design is relevant to comparing assigned groups, but the reported primary population excluded participants who did not meet the specified medication, surgical-complication, and measurement conditions. Data from one site were also excluded, for a reason not fully reported in the registry record. These features constrain interpretation of the posted estimates.

Secondary results broaden the description of postoperative pain and rescue-medication use, but the registry lists many outcomes and analyses and does not report a multiplicity strategy. They therefore provide context rather than a set of independent confirmations. The safety counts likewise describe reported events but are not, by themselves, a complete comparative safety assessment. Overall, the record supports a careful description of the estimates and their uncertainty, not a definitive conclusion about clinical benefit or harm.

18. Why This Trial Matters Statistically

This trial illustrates why a registry result should be read as a set of connected statistical choices rather than as a single p-value. The primary outcome is a patient-reported continuous measure, summarized with least-squares means and standard errors. Interpreting its group comparisons requires attention to the analysis population, the model, uncertainty, and the direction of the scale. Here, the registry gives enough information to describe the endpoint and group estimates, but not enough to reproduce the sponsor’s analysis fully.

The discrepancy between the simple recalculations and the sponsor’s reported p-values is a practical lesson in the limits of summary-statistic reconstruction. The calculations are transparent checks, yet they cannot incorporate unreported model details or participant-level information. Where the record marks a discrepancy, the sponsor’s own analysis takes precedence; the recalculation remains useful for showing how the posted summaries compare under a simpler method, not for adjudicating the conflict.

The trial also demonstrates the importance of distinguishing statistical evidence from clinical importance. A confidence interval describes uncertainty in an estimated difference, while a p-value addresses compatibility with a null model. Neither establishes whether a difference is important to patients. The registry does not report a threshold for clinically important change on the pain scale.

Finally, a broad set of endpoints and analyses makes pre-specification and multiplicity especially consequential. Without a reported testing strategy, secondary findings should not be treated as independent confirmation. Transparent reporting of population definitions, missing-data methods, model details, and analysis hierarchy would make the evidence easier to assess. These are general lessons in interpreting clinical trial registries, and they are particularly relevant to the incomplete statistical detail in this record.

19. Limitations

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

Several limitations are specific to the available record. First, the primary endpoint results are reported as least-squares means and standard errors, but the registry does not give the model specification or adjustment variables. The simple recalculations use approximate standard deviations derived from those standard errors and do not reproduce the sponsor’s ANOVA. The recalculated confidence intervals and p-values therefore should not be mistaken for sponsor-reported results.

Second, the sponsor-reported primary results contain a discrepancy with the recalculations. The registry lists two p-values for the 300 mg versus placebo pair and duplicate p-values for the 150 mg versus placebo pair, without explaining why. The reason for the data exclusion at one site is also truncated after “Good Clinical.” These reporting gaps prevent a full account of how the primary results were obtained.

Third, the modified intent-to-treat population is restricted to participants who took medication at both specified preoperative times, had no complications during herniorrhaphy, and had the primary measurement. The registry does not describe the participant flow, missing-data methods, or sensitivity analyses needed to evaluate the effects of these restrictions. The enrollment entry is 425, while endpoint and safety summaries use their own group counts; the record does not explain every difference in population accounting.

Fourth, many outcomes and analyses are listed, but no multiplicity strategy or analysis hierarchy is reported. The registry does not establish which secondary comparisons were planned as confirmatory. It also does not report a clinically important difference threshold, the original sample-size rationale, or planned interim analyses. These limitations do not invalidate the posted summaries, but they restrict the strength and scope of conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Surgical Pain After Inguinal Hernia Repair (SPAIHR) — NCT00551135.
• Registry record last updated 2021-01-25; status last verified 2010-06.
• Results first posted 2010-07-15.
• 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

NCT00551135, titled Surgical Pain After Inguinal Hernia Repair (SPAIHR), is a completed Phase 3 randomized, double-blind, parallel-group dose-ranging study. It compared pregabalin 50 mg, 150 mg, and 300 mg with placebo as adjunctive treatment for postoperative pain after primary inguinal hernia repair. The registry lists enrollment of 425 and identifies 24-hour worst pain on the modified Brief Pain Inventory-Short Form as the primary endpoint.

The primary analysis used a modified intent-to-treat population with specified preoperative medication, surgical-complication, and endpoint-measurement requirements. Posted group estimates are least-squares means with standard errors. Simple unadjusted recalculations differ from the registry’s reported analyses; for the 300 mg versus placebo comparison, the registry lists two p-values without explanation. The sponsor’s own analysis takes precedence. The record does not report enough detail on multiplicity, missing-data handling, model specification, or the site exclusion to resolve these limitations.