Lumbar Plexus vs Quadratus Lumborum Block in Post-operative Pain Following Total Hip Replacement: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lumbar Plexus vs Quadratus Lumborum Block in Post-operative Pain Following Total Hip Replacement (NCT03801265), a randomized phase 4 study. The primary outcome is Pain at Rest After Surgery.

2. Clinical Question

The trial is framed as an active-comparator non-inferiority study: it compares a new or alternative regional block with an established block rather than with no block or placebo. The study summary describes concerns about the complexity and potential complications of lumbar plexus block, and reports that QL3 block is routinely performed at the institution. Those statements explain the investigators’ rationale; they do not themselves establish comparative outcomes.

To establish non-inferiority statistically, the analysis needs a prespecified margin defining how much worse the alternative could be while still meeting the study’s criterion. That margin is not reported in the registry record. The primary comparison therefore describes the observed scores and uncertainty, but the posted information does not allow a complete assessment of whether the prespecified non-inferiority criterion was met.

3. Trial Design

The registry describes a prospective, randomized, double-blind, parallel-group, active-comparator, non-inferiority study. It is listed as phase 4 and completed. Enrollment was 46, with 23 participants reported in each arm for the primary outcome. The brief summary says the investigators planned to enroll 40 subjects, 20 in each group; the registry record does not explain the difference between that planned enrollment and the reported enrollment.

The two groups received lumbar plexus block or quadratus lumborum type 3 block. Both arm descriptions specify 0.5% ropivacaine 100 mg (20 ml). The record labels the allocation randomized and masking double, but further details about how randomization was generated, how allocation was concealed, or who was masked are not reported in the registry record.

The primary outcome was resting pain 6 hours after surgery. Secondary outcomes included pain during physical therapy, opioid consumption, walking time, block procedure duration, postoperative quadriceps weakness, and consumption of several other analgesics. The record lists 19 outcome measures and 19 analyses, while numerical summaries are available for the primary outcome and some secondary outcomes. Details for outcomes not represented by those summaries are not reported in the registry record.

The study summary states that the trial was intended to investigate whether QL3 block was non-inferior to lumbar plexus block. The non-inferiority margin, the original sample-size justification, and the planned analysis population are not reported in the registry record. No assumptions about these aspects can be inferred from the observed enrollment or from the retrospective planning illustrations.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Pain at Rest After Surgery, measured over 6 hours after surgery.

The primary endpoint is pain at rest 6 hours after surgery, measured as a score on a Visual Analog Scale from 0 to 10. The registry description defines 0 as no pain and 10 as the worst pain, and states that higher scores indicate worse outcomes. The posted group summaries are means with standard deviations: 3.4 (3.0) for lumbar plexus block and 3.6 (1.9) for quadratus lumborum type 3 block, with 23 participants in each group.

A pain score is a continuous outcome in the registry’s analysis classification, so the group means describe average reported pain and the standard deviations describe variation among participants. A resting measure addresses pain in a particular setting and at a particular assessment time; it does not by itself describe pain during movement, later recovery, or the complete postoperative experience. The registry also identifies pain during physical therapy as a separate secondary outcome.

General: selecting a specified time point and measure helps make the principal comparison clear and reduces the temptation to choose a result after seeing the data. The registry record identifies this primary measure and time point. It does not report the non-inferiority margin or additional details about how the pain assessment was administered, so those elements cannot be evaluated from the record.

7. Results Posted in the Registry

• Quadratus Lumborum Type 3 Block: mean 3.60 versus 3.40 on control; difference 0.20 (95% CI -1.25 to 1.65), standardized effect d = 0.08; z-test p = 0.787.

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 During Physical Therapy

• 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:
  • Quadratus Lumborum Type 3 Block: mean 4.20 versus 4.30 on control; difference -0.10 (95% CI -1.25 to 1.05), standardized effect d = -0.05; z-test p = 0.865.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Quadratus Lumborum Type 3 Block and the control. The interval gives the range of effects that remain compatible with the data.

Total Opioid Consumption During 24 Hours After Surgery

• 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:
  • Quadratus Lumborum Type 3 Block: mean 14.70 versus 14.00 on control; difference 0.70 (95% CI -5.09 to 6.49), standardized effect d = 0.07; z-test p = 0.813.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Quadratus Lumborum Type 3 Block and the control. The interval gives the range of effects that remain compatible with the data.

Postoperative Time to Accomplish Walking 100 Feet

• 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:
  • Quadratus Lumborum Type 3 Block: mean 1,358 versus 1,449 on control; difference -90.80 (95% CI -517.59 to 335.99), standardized effect d = -0.12; z-test p = 0.677.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Quadratus Lumborum Type 3 Block and the control. The interval gives the range of effects that remain compatible with the data.

The numerical secondary outcomes with posted group summaries cover pain during physical therapy, opioid consumption during the first 24 hours after surgery, and time to accomplish walking 100 feet. Across these measures, the recalculated point estimates are relatively close in scale to their group summaries, while their intervals extend across values on both sides of no difference. The registry also identifies other secondary outcomes, including procedure duration, postoperative quadriceps weakness, and consumption of additional analgesics; results for those outcomes are not reported in the registry record.

The overall pattern does not show an obvious, consistent separation between the blocks across the numerical secondary measures. It is broadly consistent with the primary comparison in that the posted estimates do not display a large, clearly resolved difference. That pattern is descriptive, not proof of equivalence, and it does not establish that the primary non-inferiority condition was satisfied. Secondary outcomes address different aspects of recovery and should not be treated as substitutes for the prespecified primary endpoint.

The registry reports Wilcoxon (Mann-Whitney) analyses for the secondary outcomes with p-values, but no effect estimates or intervals for those analyses. The unadjusted recalculations provide a separate view from the posted means and standard deviations. Multiple outcomes create multiple opportunities for apparently notable results to arise by chance. Unless a multiplicity strategy was prespecified and reported, individual unadjusted secondary p-values carry less weight than a result from a clearly defined primary analysis. The multiplicity plan is not reported in the registry record, so the secondary tests should be interpreted as exploratory rather than as a collection of independent confirmatory findings.

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

• Pain During Physical Therapy
• Total Opioid Consumption During 24 Hours After Surgery
• Postoperative Time to Accomplish Walking 100 Feet
• Block Procedure Duration
• Patients With Postoperative Quadriceps Weakness
• Total Acetaminophen Consumption During 24 Hours After Surgery
• Total Celecoxib Consumption During 24 Hours After Surgery
• Total Ketorolac Consumption During 24 Hours After Surgery

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports group means and standard deviations for continuous outcomes. A mean is the arithmetic average of the observations in a group. A standard deviation describes how spread out those observations are around the mean; it is not the uncertainty in the estimated mean itself. The group sizes matter when estimating how precisely a mean or a difference in means is known.

What does the recalculated mean difference represent?

General: a mean difference is formed by subtracting one group mean from the other, with the order of subtraction defining the sign. The recalculated comparison uses the QL3 mean as the first group and the lumbar plexus mean as the reference, so the posted estimate of 0.2 represents the QL3 mean minus the lumbar plexus mean. A positive value means the QL3 group mean is higher on this scale; because higher pain scores are defined as worse outcomes, that direction corresponds to a higher average pain score. This is an unadjusted comparison based on the posted group summary statistics, not an adjusted model or a replacement for the registry’s analysis.

The recalculated unadjusted p-value is 0.787. General: a p-value describes how compatible data are with a specified null model under the assumptions of a test; it is not the probability that the null hypothesis is true, nor a measure of the size or importance of an effect. A large p-value does not demonstrate that two treatments are equivalent or that a non-inferiority condition has been met.

Why is the registry’s test different?

The registry identifies the sponsor-reported method as Wilcoxon (Mann-Whitney) and reports p = .770 for the primary outcome. This rank-based method compares the relative ordering of observations between groups rather than directly testing the difference between arithmetic means in the way the simple recalculation does. The reported analysis has no posted estimate, confidence interval, or confidence level in the registry record. Therefore, its p-value cannot be used to recover the size or precision of the primary mean difference.

The recalculation and the sponsor-reported test should not be treated as interchangeable. They use different statistical approaches, and the recalculation is based only on summary values. The registry record does not report whether the sponsor’s test was adjusted for any factors, how missing outcome observations were handled, or which analysis population was used. Those details should not be inferred.

How does non-inferiority differ from testing for a difference?

General: a conventional difference test asks whether the data provide evidence that two groups differ. A non-inferiority analysis instead asks whether the alternative treatment is no worse than the comparator by more than an acceptable prespecified amount. That acceptable amount is the non-inferiority margin. The margin must be set in advance and interpreted in relation to the outcome and clinical context; otherwise, a reader cannot determine what degree of difference the study was designed to rule out.

The registry labels the sponsor analysis as non-inferiority, but does not report the margin, the analysis estimate, or its interval. The label identifies the intended type of question, but the available numerical result is not enough to verify that the criterion was satisfied. The recalculated mean-difference interval is descriptive of a simple unadjusted comparison; it is not a substitute for the missing sponsor analysis details or the missing margin.

Why does dispersion matter?

General: variability among participants affects how precisely a group average and between-group comparison can be estimated. When individual outcomes vary substantially, a similar number of observations generally gives less precise estimates than when outcomes are more tightly clustered. The standard deviations show that individual primary scores varied within both arms. The uncertainty interval for the mean difference reflects both the group means and their variability, along with the group sizes, under the assumptions of the recalculation.

Standard deviations and confidence intervals answer different questions. A standard deviation describes observed spread among participants. A confidence interval describes uncertainty about an estimated quantity under a statistical procedure. One should not read the standard deviation as a range in which most treatment effects are expected to lie, or use it alone to decide whether an observed difference is clinically meaningful.

What can and cannot be inferred from the analysis?

The registry gives a randomized, double-blind design and two treatment groups, but it does not report randomization details, allocation concealment, masking procedures, missing-data methods, analysis populations, or a full statistical analysis plan. It also does not report the confidence level for the recalculated interval. General: randomization can support a fair comparison when carried out and analyzed as intended, while masking can reduce some forms of assessment or behavior bias. Those design labels do not resolve questions about implementation or missing information.

The primary endpoint is a continuous score, but the registry’s own reported method is rank-based. This can be appropriate for analyzing outcome distributions without relying on the same assumptions as a mean-based test, but the record does not explain why that method was selected or provide distributional diagnostics. The recalculated comparison is specifically an unadjusted mean-based analysis from summary statistics. Its role is supplementary: it gives a transparent mean difference and interval, while the sponsor’s reported method remains the registry’s stated analysis.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 0.2, with an interval from -1.251 to 1.651. Because the interval includes zero, the unadjusted recalculation is compatible with values in which the QL3 mean is lower than the lumbar plexus mean, as well as values in which it is higher. Its span also indicates that the point estimate should not be read as a precise measure of the group difference. The registry record does not identify the interval’s confidence level, so a confidence percentage should not be assigned to it.

General: a confidence interval expresses the range of effect estimates that are reasonably compatible with the observed data and the method’s assumptions. It gives more information about magnitude and precision than a p-value alone. A narrow interval indicates greater precision than a wide one, while an interval that crosses zero for a difference leaves uncertainty about the direction of the difference. An interval does not show the probability that the true value lies within its particular endpoints.

For a non-inferiority question, precision must be judged against the non-inferiority margin, not just against zero. If the interval extends beyond the unacceptable boundary, it cannot rule out a loss greater than the margin. Because the margin is not reported in the registry record, the primary interval cannot be used to determine whether the non-inferiority requirement was met. The sponsor’s own analysis also lacks a posted estimate and interval, which further limits direct evaluation of its precision.

The primary outcome groups each include 23 participants. With this amount of information, the data may leave meaningful uncertainty even when the group means are close. The interval should therefore be read alongside the point estimate, the scale definition, and the missing non-inferiority criterion, rather than as evidence that the treatments have identical effects.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations express the number of participants per arm for the continuous outcomes. They are not totals across both groups and are not total event counts. The record’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record; these illustrations are separate from the trial’s original design.

The 80% power column represents the planned number of participants per arm under those assumptions for an analysis to have an 80% chance of detecting the specified effect, if that effect and the assumptions were correct. The 90% column describes the corresponding planning target for a 90% chance. These are design calculations, not estimates of what happened in the completed trial. This is not observed power.

The rows labeled as planning for 100%, 75%, and 50% of the observed effect explore how the target effect size affects the required sample. For the primary outcome, the planning figures range from 2,475 to 9,898 participants per arm for 80% power and from 3,313 to 13,250 participants per arm for 90% power across those effect assumptions. These calculations are driven by the small observed mean difference and the variability in the posted summaries; they should not be interpreted as a recommended sample size for a future study without independent clinical and design decisions.

Smaller target effects require more participants because they are harder to distinguish from random variation. The illustrations also assume that the observed effect is a useful basis for planning, an assumption that can be unstable when estimated from a small study. The original planned enrollment was 40 participants, while reported enrollment was 46; the registry record does not give the original sample-size rationale that reconciles the planning illustrations with the trial’s design.

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 = 2.511.
2. n = 2 × (1.96 + 0.842)² × 2.511² / 0.200² = 2,474.4, rounded up to 2,475 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 <- 2.51097590589794                     # 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(3801265)
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 = 2,475 (80% power), 3,313 (90% power)
 75% of observed effect: n per arm = 4,399 (80% power), 5,889 (90% power)
 50% of observed effect: n per arm = 9,898 (80% power), 13,250 (90% power)
power.t.test: 2475.3 
Simulated power at n = 2,475 per arm: 0.801 (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’s own primary analysis is identified as Wilcoxon (Mann-Whitney), with p = .770 and a non-inferiority label. It does not report the sponsor analysis’s effect estimate or confidence interval. The recalculated result is a simple unadjusted comparison of posted means: a QL3-minus-lumbar-plexus difference of 0.2, an interval from -1.251 to 1.651, and an unadjusted p-value of 0.787.

These results are not identical because they arise from different methods: the sponsor’s reported test is rank-based, while the recalculation uses mean-based summary statistics. Their p-values are close, but similar p-values do not make the procedures equivalent or establish non-inferiority. The recalculation adds a mean difference and an uncertainty interval that are not posted for the sponsor analysis; it should be read as a complementary descriptive calculation, not as a correction to the registry analysis.

The discrepancy indicator is false, but that does not remove the distinction between the methods or supply the missing non-inferiority margin. The sponsor-reported p-value cannot establish that the non-inferiority criterion was met without the margin and an appropriate estimate with uncertainty. The registry record does not report enough detail to compare the sponsor’s analysis population, missing-data approach, or model with the recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 19 outcome measures and 19 analyses, including a primary outcome and secondary outcomes. A large set of outcomes can raise a multiplicity concern: when many statistical tests are conducted, the chance of at least one apparently unusual result can increase. General: investigators can address this by defining a hierarchy of outcomes, adjusting statistical thresholds, or clearly designating secondary analyses as exploratory. The registry record does not report whether any such strategy was planned or used.

The primary endpoint is identified, which helps distinguish the main question from secondary measures. However, the non-inferiority margin and full statistical analysis plan are not reported in the registry record. The record also does not report whether the primary endpoint, analysis method, or outcome hierarchy was changed after the study began. No change should be assumed either way.

Missing-data handling is not reported in the registry record. The posted primary group sizes are 23 per arm, but the record does not explain whether every randomized participant had an observed primary outcome, whether any observations were excluded, or how incomplete secondary outcomes were handled. The analysis population—such as whether the sponsor analyzed all randomized participants or a subset—is also not reported. These omissions matter for non-inferiority studies because decisions about inclusion and missing observations can influence how much apparent similarity is observed.

Other details not reported in the registry record include the randomization sequence method, allocation concealment, masking procedures, protocol deviations, and whether models adjusted for baseline characteristics or other factors. The record gives an outcome measure and a sponsor-reported test, but not enough information to reconstruct the full analysis. This limits assessment of the risk of selective outcome reporting and the robustness of the sponsor’s conclusions.

These are reporting limitations, not proof that the methods were inappropriate. They identify what a reader cannot verify from the registry record. Without additional documentation, the posted results can be described and their uncertainty discussed, but the planned handling of multiplicity, missing data, and analysis populations cannot be confirmed.

16. 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.

The serious adverse event figures report 23 participants at risk in each group and zero participants affected by a serious adverse event in either group. The record also reports 23 participants at risk in each group and zero affected by other adverse events. No deaths are reported in either arm, and no serious adverse event terms are listed.

These are counts from the registry record for the reported study groups. Zero reported events means that no affected participants were recorded in these categories in the posted figures; it does not establish that an event is impossible or that the procedures have no safety risks. With 23 participants per arm, the safety observations are limited to the participants and period represented by the record.

The study summary discusses potential complications associated with lumbar plexus block and theoretical advantages of inter-fascial administration. Those are background rationale statements, not observed event counts. The registry’s zero counts do not demonstrate that QL3 avoids those potential complications or that the two blocks have equivalent safety. The adverse-event categories, collection details, and observation period are not reported in the registry record, limiting further interpretation.

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

The registry describes a randomized, double-blind comparison of lumbar plexus block and QL3 block in participants undergoing total hip replacement. For resting pain 6 hours after surgery, the group means were 3.4 and 3.6, respectively. The recalculated mean difference was 0.2, with an interval from -1.251 to 1.651. The registry’s own rank-based analysis reports p = .770 and is labeled non-inferiority.

These findings describe the available outcome data; they do not establish that the blocks are equivalent, that QL3 is non-inferior, or that either block is preferable. A non-inferiority conclusion requires a prespecified margin and a suitable estimate with uncertainty that can be judged against that margin. The margin is not reported, and the sponsor analysis’s estimate and interval are not reported. A non-significant p-value is not evidence that clinically important differences have been ruled out.

The primary endpoint is a single resting-pain assessment at a specified postoperative time. It cannot represent all dimensions of pain, function, recovery, or safety. The secondary outcomes offer additional measures, but their statistical interpretation is limited by missing information about multiplicity and by the absence of sponsor-reported effect estimates and intervals. The adverse-event counts are zero in both arms in the posted categories, but the small group sizes and incomplete reporting prevent broad safety conclusions.

The study summary describes a rationale for evaluating QL3 as an alternative to lumbar plexus block. The posted numerical results can inform discussion of the measured outcomes, but they do not confirm the hypothesized benefits or eliminate the potential risks described in the rationale. Important protocol and analysis details, including the original sample-size justification, missing-data methods, and analysis populations, are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority label is not enough to interpret a result. The central statistical question is not simply whether a conventional test finds a difference. It is whether the uncertainty around the treatment contrast excludes a loss larger than an acceptable prespecified margin. Without that margin, even a p-value from an analysis labeled non-inferiority cannot show the reader where the decision boundary lies.

It also demonstrates the distinction between a sponsor-reported analysis and a transparent recalculation from summary statistics. The registry’s Wilcoxon (Mann-Whitney) result is rank-based, while the recalculation estimates an unadjusted difference between means. Reporting both methods can help readers understand what each says, but their outputs are not interchangeable. A p-value alone obscures the size and precision of an effect; an estimate and interval make those features more visible.

The small enrollment and the broad recalculated primary interval emphasize the importance of precision. A close pair of means is not the same as evidence that the difference is acceptably small. Likewise, zero recorded adverse events do not establish that risks are absent. The trial therefore provides a useful example of how design labels, outcome summaries, uncertainty, and missing reporting details must be considered together rather than treating one result as decisive.

19. Limitations

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

The primary limitation for interpreting the stated non-inferiority question is that the margin is not reported in the registry record. The sponsor’s analysis is labeled non-inferiority, but the record provides only a p-value, without an effect estimate or interval. This prevents direct evaluation of whether the observed uncertainty falls within an acceptable boundary.

The recalculated mean difference and interval are based on posted summary statistics and are unadjusted. They do not reproduce the sponsor’s Wilcoxon (Mann-Whitney) analysis and should not be treated as a substitute for individual-participant data or a full statistical analysis. The confidence level for the recalculated interval is not stated in the registry record.

Reported enrollment was 46, while the brief summary says the investigators planned 40 participants. The original sample-size assumptions and justification are not reported, so the reason for the difference cannot be determined. The planning illustrations based on observed effects are not the trial’s original design calculations.

The registry record does not report missing-data procedures, analysis populations, randomization implementation, allocation concealment, or detailed masking procedures. It also does not report a multiplicity plan, the full statistical analysis plan, or whether the prespecified approach changed. These omissions make it difficult to assess how robust the results are to analytic choices or incomplete outcome data.

Finally, the group sizes are limited, the primary result concerns one pain measure at one time point, and the safety record reports no affected participants in either arm. Results for several listed secondary outcomes are not reported in the registry record. These features constrain conclusions about broader recovery outcomes and uncommon adverse events.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Lumbar Plexus vs Quadratus Lumborum Block in Post-operative Pain Following Total Hip Replacement — NCT03801265.
• Registry record last updated 2021-07-15; status last verified 2021-06.
• Results first posted 2021-07-15.
• 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

The registry describes a completed phase 4, randomized, double-blind, parallel-group active-comparator non-inferiority study of lumbar plexus block versus quadratus lumborum type 3 block after total hip replacement. It reports 46 participants enrolled, with 23 participants in each group for the primary outcome. Both block descriptions specify 0.5% ropivacaine 100 mg (20 ml).

The primary outcome was resting pain 6 hours after surgery on a 0-to-10 Visual Analog Scale. Group means were 3.4 for lumbar plexus block and 3.6 for QL3 block. The sponsor-reported Wilcoxon (Mann-Whitney) analysis gives p = .770 and is labeled non-inferiority. An unadjusted recalculation gives a mean difference of 0.2 with an interval from -1.251 to 1.651. The non-inferiority margin is not reported in the registry record, limiting interpretation of the stated study question.

Posted adverse-event figures report no affected participants and no deaths in either group. Important details on the statistical plan, missing data, analysis populations, and multiplicity are not reported in the registry record.