Management of Postoperative Pain After Total Knee Replacement.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Management of Postoperative Pain After Total Knee Replacement. (NCT01163214), a randomized phase 4 study. The primary outcome is Post-Operative Pain.

2. Clinical Question

The trial focused on a direct comparison of two postoperative pain-management approaches in people undergoing the same type of surgery. The primary outcome captures reported pain at a specified postoperative time, rather than pain over the entire hospital stay or at later follow-up. The registry record also identifies secondary questions about pain among participants who received their allocated treatment, narcotic use, straight-leg raise, hospital length of stay, and postoperative neurological changes. The reported findings should therefore be read as answers to specific measured outcomes and time points, not as a complete account of every aspect of recovery.

3. Trial Design

This was a Phase 4, randomized, parallel-group study with no masking. The two groups were assigned to nerve block or periarticular injection. The record reports an enrollment of 160, with 79 participants in the nerve-block group and 81 in the periarticular-injection group for the primary intention-to-treat outcome. The two group descriptions distinguish the regional block procedures from an injection combination administered before skin closure.

The study began in 2010-07, and primary completion is recorded as 2013-06. Its status is completed. The record describes the purpose as comparing two methods of postoperative pain management in patients undergoing total knee replacement. It does not report the original sample-size justification or the planned statistical analysis in enough detail to establish what assumptions informed the trial's design. Those aspects should not be inferred from the retrospective planning illustrations based on observed effects.

Randomization supports a comparison between assigned groups, while the parallel design means participants were followed in one assigned group rather than receiving both approaches in sequence. The absence of masking is relevant when considering a participant-reported pain measure: participants and care teams were not masked according to the record, and the outcome depends on reported experience. The registry record does not report whether outcome assessors were separately masked.

The primary outcome population is identified as intention to treat. A per-protocol pain outcome is also listed as a secondary result, using participants who received the allocated treatment. These populations answer related but not identical questions: the intention-to-treat analysis retains the assignment-based comparison, whereas a per-protocol analysis focuses on those who received the assigned approach. The registry record does not report further detail on exclusions, deviations, or missing-outcome handling.

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

Analysis population for the primary outcome, as defined in the registry: Intention to treat analysis

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 Post-Operative Pain, measured over Afternoon on post-operative Day 1, approximately 14:00.

The primary endpoint is postoperative pain measured on a linear analog scale from 0, meaning no pain, to 10 points, meaning worst possible pain. The recorded measurement time is the afternoon of post-operative Day 1, approximately 14:00. The registry reports the group mean and standard deviation for the intention-to-treat population.

A pain score is a patient-reported measure of an experience that is not directly captured by an objective laboratory measurement. A common scale provides a consistent way to record participants’ ratings and compare the distributions of scores between randomized groups at the specified time. The mean describes the group’s average rating; the standard deviation describes how spread out individual scores are around that average. Neither statistic alone describes every participant’s experience.

Timing matters to interpretation. These results concern pain at a particular point after surgery, not pain at all postoperative times or a summary across the full recovery period. The registry record does not report a clinically important difference threshold for this scale, so it does not establish how large a difference would be meaningful to patients. It also does not report the exact handling of missing pain measurements. The endpoint can therefore be interpreted as a comparison of recorded average pain scores at the stated time, with those limits in mind.

7. Results Posted in the Registry

• Periarticular Injection: mean 3.00 versus 2.90 on control; difference 0.10 (95% CI -0.61 to 0.81), standardized effect d = 0.04; z-test p = 0.784.

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.

Pain Scores in the Per-protocol Subset (Participants Who Received the Allocated Treatment)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Periarticular Injection: mean 3.10 versus 2.90 on control; difference 0.20 (95% CI -0.54 to 0.94), standardized effect d = 0.09; z-test p = 0.594.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Periarticular Injection and the control. The interval gives the range of effects that remain compatible with the data.

Length of Stay in Hospital

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Periarticular Injection: mean 2.44 versus 2.84 on control; difference -0.40 (95% CI -0.74 to -0.06), standardized effect d = -0.39; z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Periarticular Injection than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the scope beyond the primary intention-to-treat pain comparison. The registry lists pain in the per-protocol subset, narcotic use, straight-leg raise, hospital length of stay, and postoperative neurological changes. The detailed numeric results available in the record include the per-protocol pain outcome and length of stay. Numerical findings for narcotic use, straight-leg raise, and neurological changes are not reported in the registry record.

The per-protocol pain comparison is generally consistent with the primary result: the group means are close, and the reported tests do not provide strong evidence of a difference. The hospital length-of-stay outcome has a different pattern, with a reported group mean difference and a nominal p-value of 0.02. These secondary findings should be considered alongside, rather than as replacements for, the primary pain result. The outcomes measure different aspects of care and recovery, so a result for length of stay does not resolve the primary question about pain at the specified time.

Unadjusted secondary tests carry less weight because multiple outcomes create multiple opportunities to observe a small p-value by chance. A multiplicity adjustment accounts for that broader testing context; the registry record does not report such an adjustment. It also does not report a hierarchy or confirmatory plan that would establish how secondary findings were intended to be interpreted. Consequently, the nominal length-of-stay result is informative as a recorded comparison but should not be treated as independently conclusive evidence.

The secondary results also differ in analysis population and outcome type. The per-protocol pain analysis focuses on participants who received allocated treatment, whereas the primary analysis is intention to treat. Length of stay is measured in days and is not a pain-scale measure. These distinctions limit how results can be combined into a single overall conclusion. The registry record does not report numerical results for every listed secondary outcome, so the complete pattern across all secondary questions cannot be assessed from the reported values.

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

• Pain Scores in the Per-protocol Subset (Participants Who Received the Allocated Treatment)
• Narcotic Use
• Straight-leg Raise
• Length of Stay in Hospital
• Number of Subjects Who Experienced Neurological Changes Postoperatively

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports group means and standard deviations for the continuous primary pain outcome. The mean is the arithmetic average of the recorded scores within a group. The standard deviation describes variability among individual scores; a larger value indicates that scores are more dispersed around the group mean. Group summaries give a useful description, but they do not show the full score distribution or how many participants had any particular rating.

What does the mean difference represent?

The recalculated mean difference is formed as the periarticular-injection mean minus the nerve-block mean. A positive value means the average score was numerically higher in the periarticular-injection group; because higher values on this scale indicate more pain, the sign describes direction rather than importance. For the primary outcome, the recalculated difference is 0.1 units. This is an unadjusted comparison based on posted summary statistics, not a model-adjusted estimate. The registry record does not report an adjusted primary effect estimate.

For continuous outcomes, comparing means is a familiar way to summarize group separation. The pooled standard deviation is used in the recalculation of standardized effect size and planning illustrations. Standardization expresses a mean difference relative to the spread of the observations, which can make the magnitude easier to compare across measures with different units. It does not establish whether a difference matters to patients. No clinical-importance threshold is reported for the pain scale.

Why are both a t-test and a rank test reported?

The registry lists a two-sided t-test and a Wilcoxon (Mann-Whitney) test for the primary comparison. A t-test evaluates evidence about a difference in group means under its statistical assumptions. A rank-based test compares the ordering of observations across groups and does not test exactly the same quantity as a mean-difference estimate. Agreement or disagreement between these tests can provide context about how sensitive the conclusion is to the choice of method, but the tests do not become interchangeable. The record gives p-values for both tests without further detail on assumptions, diagnostics, or whether one was designated as the principal inferential test.

A two-sided test considers departures in either direction rather than only a prespecified direction. A p-value describes how compatible the observed data are with a specified null model, under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value should be read together with the effect estimate and its uncertainty.

What role does the confidence interval play?

A confidence interval gives a range of estimates compatible with the data and the method used to calculate it. For the primary mean difference, the interval crosses zero. Zero represents no difference in the group means under this contrast. The interval therefore indicates that the data do not pin down the direction of a possible mean difference. It is not evidence that the true difference must be zero. The interval’s breadth also matters: a range that permits effects on both sides of zero leaves meaningful uncertainty about the magnitude and direction.

The displayed recalculation is based on the posted group summary statistics and is unadjusted. Its p-value is not exactly the same as the registry’s reported t-test p-value. The discrepancy flag is false, and the registry’s own analyses remain the sponsor-reported results. The recalculation is best treated as a transparent companion to those results, rather than a replacement for the analysis specified and conducted by the sponsor.

Why can over-dispersion matter in general?

In general, over-dispersion means that observed variability is greater than a statistical model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow, making evidence appear more precise than it is. For a continuous outcome summarized with group means and standard deviations, the observed spread is directly relevant to uncertainty in the group comparison. The registry record does not report a model that assumes a particular dispersion level or an over-dispersion adjustment for the primary outcome. This general issue should not be mistaken for a reported problem in this trial.

For the length-of-stay outcome, the registry again reports group means and standard deviations, and a two-sided t-test p-value. Length of stay is recorded in days. Its interpretation as a mean difference relies on the outcome summaries and test, and the registry record does not report further model details or adjustment for other variables. The observed group summaries do not establish why lengths of stay differed.

How should the planning illustrations be understood?

The sample-size illustrations use observed effects as planning inputs and show the participants per arm associated with stated power targets under listed assumptions. They are not results from the randomized comparison and should not be read as evidence that the study had a particular probability of detecting its observed result. A planning calculation depends on the effect chosen, the assumed variability, allocation, significance level, and statistical approximation. The original design assumptions for this trial are not reported in the registry record. The retrospective illustrations therefore cannot establish whether the original trial was planned around the observed effect or whether its design had a particular power for the primary endpoint.

Across these methods, the main distinction is between describing the observed data, estimating an effect with uncertainty, and testing a statistical hypothesis. Group means and standard deviations describe the recorded scores; a mean difference describes the contrast; a confidence interval conveys its precision; and a p-value summarizes compatibility with a null model under a test. None of these alone determines clinical importance. The registry does not report the protocol-level details needed to resolve all choices about analysis populations, missing data, outcome hierarchy, or multiplicity.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 0.1 units, comparing periarticular injection with nerve block. Its confidence interval extends to both sides of zero. That interval is central to interpretation because the point estimate alone gives only one estimate from the data, while the interval conveys the uncertainty around it. Since the interval includes zero, the data do not determine the direction of a mean difference with confidence under this calculation.

The interval also allows differences that are not exactly zero. It should not be reduced to a yes-or-no statement about whether a difference exists. The registry record does not provide a threshold for a clinically important change in pain score, so the interval cannot be classified against such a threshold. It also does not report an equivalence margin. A confidence interval crossing zero is not, by itself, proof of equivalence.

Precision depends on the amount of information in the data and the variability of the outcome. The reported standard deviations show that individual pain ratings vary within each group. The comparison therefore concerns group averages despite variation among participants. The group means are close, but the confidence interval indicates that the estimate is not precise enough to settle the direction of a possible difference.

The reported sponsor p-values provide another summary of evidence, but they do not replace the effect estimate or interval. A p-value does not say how much uncertainty remains in the estimate, and a non-small p-value does not establish that there is no effect. Read together, the result is a small observed mean difference with uncertainty spanning zero, rather than a definitive demonstration that the groups are identical.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For continuous outcomes such as these, the figures are participants per arm, not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm associated with an 80% chance of detecting the specified effect under those assumptions, if the assumed effect and model are correct. The 90% power column applies the same idea at a higher target chance of detection. These are planning targets, not guarantees about a future study’s result. The values are conditional on the assumptions and effect size used for each calculation.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. This is expected: smaller differences are harder to distinguish from random variation than larger differences when other assumptions are held fixed. The observed effect is particularly small for the primary pain outcome, so the planning figures based on that effect are large. This is not observed power: it does not describe the probability that the completed trial detected its true effect, and it should not be used to interpret the observed p-value as a measure of trial success.

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 = 0.100; pooled standard deviation σ = 2.301.
2. n = 2 × (1.96 + 0.842)² × 2.301² / 0.100² = 8,310.7, rounded up to 8,311 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 <- 0.1                      # observed difference in means
sigma <- 2.30090791106247                     # 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(1163214)
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 = 8,311 (80% power), 11,126 (90% power)
 75% of observed effect: n per arm = 14,775 (80% power), 19,779 (90% power)
 50% of observed effect: n per arm = 33,243 (80% power), 44,503 (90% power)
power.t.test: 8311.6 
Simulated power at n = 8,311 per arm: 0.798 (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 registry reports the sponsor’s own primary analyses as a two-sided t-test with p = 0.76 and a Wilcoxon (Mann-Whitney) test with p = 0.59. The recalculated unadjusted comparison uses the posted group means, standard deviations, and group sizes to estimate a mean difference of 0.1 units, with an unadjusted p-value of 0.784. The recalculation is a simple summary-statistic comparison and is not a substitute for the sponsor’s analysis.

The registry’s reported p-values are close in their broad interpretation: they do not provide strong evidence of a difference in the primary pain outcome at the stated assessment. The sponsor’s tests and the recalculation may differ because they use different procedures or details that are not reported in the registry record. The discrepancy flag is false, but that does not make the recalculation the definitive analysis. The sponsor’s reported results should be treated as the trial’s own analysis, while the recalculation offers a transparent, unadjusted comparison derived from the posted summaries.

For the per-protocol pain outcome, the sponsor reports p-values of 0.78 for the two-sided t-test and 0.58 for the rank test; the corresponding unadjusted recalculation is also based on summary statistics. For length of stay, the reported two-sided t-test p-value is 0.02, matching the unadjusted recalculation’s p-value. These secondary results answer distinct questions and do not alter which outcome was designated primary.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and several secondary outcomes. Multiple statistical comparisons can raise the chance of at least one apparently notable result occurring by chance, especially when tests are considered without adjustment. The record does not report whether a multiplicity correction was planned or applied, nor does it report a hierarchy governing the interpretation of secondary outcomes. The reported secondary p-values should therefore be regarded as nominal unless an adjustment is documented elsewhere in the registry record.

The primary outcome is described as an intention-to-treat analysis, and the per-protocol pain outcome is separately identified among participants who received the allocated treatment. This distinction is important. Intention-to-treat analysis generally preserves comparison according to randomized assignment, while per-protocol analysis restricts attention to those who followed the allocated treatment. In general, restricting a randomized comparison can introduce differences between the included participants that are not due to random assignment. The record does not report enough detail to assess the reasons for treatment deviations or how they were handled.

The missing-data approach for the primary pain outcome and secondary outcomes is not reported in the registry record. It is not reported whether missing measurements were imputed, whether analyses used only participants with recorded outcomes, or whether sensitivity analyses examined alternative assumptions. The reported analysis group sizes indicate the number included in the listed outcome summaries, but do not explain the status or handling of any unrecorded measurements.

The registry record also does not report the original statistical analysis plan, interim analyses, or detailed prespecification of the tests. These omissions limit assessment of whether analysis choices were set before results were known. The recorded primary endpoint and the reported tests can still be described, but unreported planning and missing-data details should not be inferred. In particular, the secondary p-value should not be treated as if it had been adjusted or prespecified in a confirmatory testing hierarchy.

These limitations affect certainty about the full analysis strategy, not the numerical values posted for the reported outcomes. Readers can distinguish the primary intention-to-treat comparison from the secondary analyses, recognize the multiple-testing context, and note that the registry does not describe missing-data methods. No claim about the adequacy of the original analysis plan can be made from the information in the registry record.

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% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute pulmonary embolism (1.3%), acute renal failure (1.3%), lumbar vertebral fracture after fall (1.3%), stroke middle cerebral artery (1.3%).

The registry reports serious adverse events in 4 participants in the nerve-block group and 0 in the periarticular-injection group. It reports other adverse events in 55 participants in the nerve-block group and 54 in the periarticular-injection group. These are counts within the group sizes listed for the safety results. The categories should not be conflated: serious events and other adverse events are reported separately.

The listed serious-event terms are acute pulmonary embolism, acute renal failure, lumbar vertebral fracture after fall, and stroke middle cerebral artery; each is accompanied by 1.3%. The registry does not provide further event-level context in the information, so the listed terms should not be used to infer causation or comparative risk. The number of deaths is not reported in the registry record.

Adverse-event counts are descriptive safety information. They do not by themselves establish that an event was caused by an intervention, and the record does not report adjudication details or the relationship of each event to treatment. The difference in recorded serious-event counts should be read with the group sizes and the limited event detail in mind, not as a definitive estimate of comparative safety.

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

The primary result describes average pain scores in the two randomized groups on the afternoon of post-operative Day 1, approximately 14:00. The means were 2.9 for nerve block and 3.0 for periarticular injection on a scale from 0 to 10 points. The recalculated difference is small and its confidence interval includes zero; the sponsor’s reported tests likewise do not provide strong evidence of a primary-outcome difference. These findings describe the recorded comparison at that time point.

They do not prove that the approaches are equivalent, that any possible difference is unimportant, or that the true difference is zero. The registry record does not report a clinical-importance threshold or an equivalence margin. A result that does not provide strong evidence against a null model is not the same as evidence that two approaches have identical effects.

The primary outcome is one measure of postoperative experience, not a complete measure of recovery. Secondary outcomes include pain among participants who received their allocated treatment and length of stay, along with other listed outcomes. The secondary length-of-stay result is separate from the primary pain comparison, and unadjusted secondary findings have to be interpreted in the context of multiple comparisons. The registry does not report numerical findings for every listed secondary outcome.

The study was randomized but unmasked. Random assignment supports comparison of the allocated groups, while lack of masking can matter for a participant-reported measure such as pain. The registry record does not report whether other outcome assessors were masked or how missing outcome data were handled. Those uncertainties should remain distinct from the reported group means and tests.

Nothing in these results alone establishes what an individual should choose or predicts an individual’s pain experience. The data are a trial-level comparison of two approaches in the enrolled population, at a specified postoperative assessment. Their interpretation is bounded by the endpoint, timing, analysis details, and uncertainty reported in the registry.

18. Why This Trial Matters Statistically

This trial is statistically useful because it puts two distinct postoperative pain-management approaches into a randomized, parallel-group comparison and records a patient-reported outcome at a defined postoperative time. A clear endpoint and time point make the contrast interpretable: the question concerns average pain ratings on the afternoon of post-operative Day 1, rather than a vague overall impression of recovery.

The result also illustrates why effect estimates and uncertainty should be read together. The observed group means are close, and the recalculated mean difference is 0.1 units, but the confidence interval crosses zero. The sponsor’s own tests are consistent with the absence of strong evidence for a primary difference, without proving equivalence. This distinction is important in clinical research: a statistically inconclusive comparison does not settle whether effects are identical or whether any difference is meaningful.

The secondary length-of-stay result highlights a separate statistical issue. A nominal result on a secondary endpoint may attract attention, but multiple comparisons and an unreported multiplicity strategy make it less definitive than a prespecified primary finding. Different endpoints also represent different dimensions of care. A result on length of stay should not be treated as a proxy for the primary pain measure.

Finally, the record makes visible the value of reporting analysis populations, outcome definitions, and safety counts, while also showing the limits created when missing-data procedures, original sample-size assumptions, and multiplicity plans are not reported. These details influence how precisely trial findings can be evaluated and how far conclusions can reasonably extend.

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 registry record has several trial-specific limitations for interpretation. The study was unmasked, and the primary endpoint is a participant-reported pain score. The record does not report whether outcome assessors were separately masked. It also does not report the exact handling of missing pain measurements, reasons for any departures from allocated treatment, or sensitivity analyses addressing those issues.

The original sample-size justification and statistical analysis plan are not reported in the registry record. The planning illustrations based on observed effects are not a substitute for original design assumptions. The record does not report whether interim analyses were conducted, or whether secondary outcomes were governed by a prespecified hierarchy or multiplicity adjustment. This makes it difficult to determine which secondary comparisons were intended as confirmatory.

Interpretation is also limited by the defined outcome and timing. The primary result concerns pain on the afternoon of post-operative Day 1, not pain across all postoperative periods. The registry record does not provide a clinically important difference threshold for the pain scale. It therefore does not allow the observed mean difference or its interval to be assessed against a stated patient-relevant threshold.

Some listed secondary outcomes do not have numerical findings reported in the registry record, limiting assessment of the full set of secondary questions. Safety information includes counts and serious-event terms, but the record does not report event attribution or detailed adjudication. The number of deaths is not reported. These limitations do not change the posted values, but they constrain conclusions about the broader clinical picture and the completeness of the analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Management of Postoperative Pain After Total Knee Replacement. — NCT01163214.
• Registry record last updated 2014-11-05; status last verified 2014-11.
• Results first posted 2014-11-05.
• 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 completed Phase 4 study randomized participants in a parallel, unmasked comparison of nerve block and periarticular injection after total knee replacement. The primary intention-to-treat endpoint was pain on a 0-to-10 linear analog scale on the afternoon of post-operative Day 1, approximately 14:00.

Mean primary pain scores were 2.9 for nerve block and 3.0 for periarticular injection. The sponsor reported two-sided t-test and Wilcoxon (Mann-Whitney) p-values of 0.76 and 0.59. The unadjusted recalculation gives a mean difference of 0.1 units, with a confidence interval that includes zero. The registry also reports selected secondary results and adverse-event counts, while several analysis details are not reported in the registry record.