Repeat Quadratus Lumborum Block to Reduce Opioid Need in Patients After Pancreatic Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Repeat Quadratus Lumborum Block to Reduce Opioid Need in Patients After Pancreatic Surgery (NCT03745794), a randomized phase 2 study. The primary outcome is Number of Participants Discharged Opioid-Free.

2. Clinical Question

The practical contrast is therefore not a block versus no block: both groups received a block before surgery. The randomized treatment difference was the addition of a second quadratus lumborum block after surgery. The registry describes the goal as reducing opioid need after pancreatic surgery, including opioid prescriptions at discharge. The primary outcome captures opioid-free status at discharge, while the secondary outcomes include opioid use, opioid-equivalent consumption, prescription size, hospital cost, and quality-of-life measures. The primary result should be read as a comparison of the two assigned care strategies on that discharge outcome, rather than as a direct measure of every aspect of pain control, opioid exposure, or later opioid use.

3. Trial Design

This is a randomized, parallel-group phase II trial sponsored by M.D. Anderson Cancer Center. The registry lists a triple masking design and enrollment of 136 participants. The trial status is completed. Its recorded start date is 2019-02-28, and its primary completion date is 2025-07-31.

Participants were assigned to one of two strategies. The usual-care arm received a quadratus lumborum block before surgery and multimodal pain control after surgery. The experimental arm received the same preoperative block and multimodal pain control, plus a second quadratus lumborum block on day 4 after surgery, followed by standard care. This active-comparator design focuses the contrast on whether adding the repeat block changes outcomes over and above the initial block and the shared postoperative care.

The registry reports 52 participants in the control arm and 53 in the experimental arm for the primary outcome. One participant is described as inevaluable for that analysis. The registry separately lists safety denominators of 52 and 54, respectively; these are the counts attached to the adverse-event reporting and should not be substituted for the primary-outcome denominators.

Eleven outcome measures and one analysis are listed in the registry record, and ten secondary outcomes are posted. The primary analysis is described as a chi-squared test comparing the proportions discharged opioid-free. Details of the randomization procedure, allocation concealment, the operational meaning of triple masking, and the specific statistical plan beyond the listed analysis are not reported in the registry record. The original sample-size justification and any interim-analysis plan are also not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 30 participants were excluded from the study before assignment to arms due to aborted surgery, discharged before 4 days after surgery or opioids free at 3rd day after surgery.

Overall Study

Analysis population for the primary outcome, as defined in the registry: one participant inevaluable for 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 Number of Participants Discharged Opioid-Free, measured over 90 days from surgery.

The primary endpoint is the number of participants discharged opioid-free. The registry describes the comparison as the proportion of patients who were opioid-free on the discharge date and gives the timeframe as 90 days from surgery. In this context, the endpoint records whether a participant was opioid-free at discharge; it does not measure the amount of opioid taken by every participant or the duration of use after discharge.

This endpoint is relevant to the trial’s stated aim because discharge prescribing and opioid use are among the outcomes the trial sought to examine. A binary outcome makes the comparison straightforward to describe: each participant is classified as opioid-free or not opioid-free at discharge, and the groups’ proportions can be compared. That simplicity also limits what the endpoint can tell readers. It does not capture variation in dose among participants who received opioids, pain intensity, or later changes in opioid use. The registry lists these and related topics among secondary outcomes, but the primary result should be interpreted specifically as opioid-free status at discharge.

The primary outcome counts are 19 of 52 in the control arm and 27 of 53 in the experimental arm. The registry states that one participant was inevaluable for analysis. The endpoint description does not explain the reason for that exclusion or provide further detail about how opioid-free status was ascertained.

7. Results Posted in the Registry

• Arm 2, Experimental Arm (2nd QL-Block): 50.9% (27/53) versus 36.5% (19/52) on control; risk difference 14.4 percentage points (95% CI -4.4 to 33.2), risk ratio 1.39 (0.89–2.18); unadjusted two-proportion z-test p = 0.137.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: participants are classified according to whether they were discharged opioid-free. The registry says the groups were compared using a chi-squared test. This test evaluates whether the observed distribution of the binary outcome across the two groups is consistent with equal proportions, under the assumptions of the test. It does not by itself describe the size of a difference, so an effect estimate and its confidence interval are useful alongside the test result.

What does the risk difference express?

The risk difference subtracts the control-group proportion from the experimental-group proportion. It expresses the contrast in absolute probability units, making it possible to see how far apart the observed group proportions are without converting them into a relative scale. The recalculated unadjusted risk difference is 0.144. A positive value indicates a higher observed proportion in the second-block arm for this outcome. The estimate is not an adjusted comparison: it is recalculated from the posted arm-level counts and does not account for additional participant characteristics.

How should the p-value be understood?

A p-value describes how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the probability that the observed pattern occurred by chance in an everyday sense. The recalculated unadjusted p-value is 0.137, while the registry reports a chi-squared p-value of 0.17. The figures come from different presentations of the comparison and should be reported as such, not treated as interchangeable estimates of effect. Neither value is below the 0.05 significance level specified for the planning illustration.

Why use a confidence interval?

A confidence interval gives a range of effect estimates that are reasonably compatible with the observed data under the method used. It communicates precision as well as direction. For this risk difference, the interval includes zero, the value corresponding to no absolute difference, and extends to both sides of zero. The point estimate is therefore not a precise stand-alone summary of what the trial established. The interval also does not assign probabilities to individual effects or guarantee that the true effect lies within its endpoints.

What do relative measures add?

The recalculation also gives a risk ratio and an odds ratio. A risk ratio compares the outcome proportions, while an odds ratio compares the outcome odds. These use relative rather than absolute scales and can answer related but distinct questions. Both recalculated measures have confidence intervals that include their respective null value. Their uncertainty is consistent with the uncertainty indicated by the risk-difference interval; none of these measures independently establishes a clear group difference. Relative measures can also be less intuitive for decisions than an absolute difference, so the scale should be made explicit whenever they are discussed.

Why might count outcomes need different methods?

Several listed secondary outcomes involve opioid-equivalent consumption or other quantities. General statistical context: count and consumption outcomes can have skewed distributions, many low or zero values, or greater variability than a simple model assumes. Over-dispersion means the variation in the data exceeds what a particular count model expects; if ignored, uncertainty estimates may be too optimistic. The registry entries summarized for the primary result do not identify the methods used for those secondary outcomes, so no particular model or adjustment can be attributed to the trial.

The primary analysis is reported as one chi-squared comparison. The registry does not provide further details about covariate adjustment, stratification, model diagnostics, or whether the analysis followed an intention-to-treat population. Those details are not reported in the registry record. The unadjusted recalculation is useful as a transparent check based on the posted counts, but it does not replace the sponsor’s analysis or supply undocumented design details.

10. Confidence Intervals and Precision

The estimated risk difference is 0.144, with a 95% confidence interval that runs from a negative value to a positive value. Because zero lies within that interval, the data are compatible with no absolute difference as well as with differences favoring either group. This breadth matters: the point estimate alone gives a more definite impression than the interval supports.

Precision is limited by the amount of information in the primary comparison. The outcome counts are 19 of 52 in the control arm and 27 of 53 in the experimental arm. With this level of information, the interval remains broad enough to include materially different interpretations of the group contrast. The registry entries do not identify a clinically important threshold, so the interval cannot be judged against a trial-defined margin for importance.

The relative effect estimates are uncertain too. The risk-ratio and odds-ratio confidence intervals include the corresponding null value, reinforcing that the analysis does not sharply distinguish a difference from no difference. Confidence intervals describe uncertainty under the statistical method; they do not resolve potential limitations in outcome ascertainment, missing data, or analysis choices.

The registry reports p = 0.17 for its chi-squared test, while the unadjusted recalculation gives p = 0.137. These are not measures of precision in the same way as a confidence interval, and neither should replace the interval-based reading of the estimated effect. The registry does not report a confidence interval for its own analysis. Overall, the result is suggestive in direction but imprecise, and should not be presented as a settled estimate of the effect of adding a second block.

11. 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 plan. The registry does not report the original design assumptions or sample-size justification. The listed figures are participants per arm, not total participants or total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect.

For each assumed effect size, the 80% power column gives the illustrative number of participants per arm that would yield an 80% chance of detecting an effect of that size under the listed assumptions, if the effect were real and the assumptions held. The 90% power column expresses the corresponding planning target for a 90% chance of detection. These are planning concepts, not probabilities that the observed result is correct.

The row based on 100% of the observed effect gives 185 participants per arm for 80% power and 248 participants per arm for 90% power. Planning for 75% of the observed effect gives 327 participants per arm for 80% power and 437 participants per arm for 90% power. Planning for 50% of the observed effect gives 726 participants per arm for 80% power and 972 participants per arm for 90% power. Smaller effects require more participants to detect under the same assumptions.

These figures are not observed power. They are prospective planning illustrations that reuse the observed effect estimate, which is itself uncertain. The figures do not show that the trial was originally designed around those targets, and the registry record does not report the trial’s original sample-size assumptions.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.365; treatment proportion p₁ = 0.509; average p̄ = 0.437.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7015 = 1.3750.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6941 = 0.5842.
4. n = (1.3750 + 0.5842)² / (0.1440)² = 185.0, rounded up to 185 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.365384615384615                          # control proportion
p1 <- 0.509433962264151                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3745794)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 185 (80% power), 248 (90% power)
 75% of observed effect: n per arm = 327 (80% power), 437 (90% power)
 50% of observed effect: n per arm = 726 (80% power), 972 (90% power)
power.prop.test: 185 
Simulated power at n = 185 per arm: 0.809 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports that the primary comparison used a chi-squared test and gives p = 0.17. A separate unadjusted recalculation from the posted arm counts gives a risk difference of 0.144 and p = 0.137. The recalculated result is a simple comparison of the posted proportions and is not a substitute for any analysis details that may have informed the sponsor’s reported result.

The record does not indicate a discrepancy flag for these results. The two p-values are close in their broad interpretation: neither is below the 0.05 significance level used in the planning illustration. The registry’s reported analysis should be identified as the sponsor’s posted analysis, while the recalculation should be described as unadjusted. Neither p-value establishes the size or clinical importance of the effect; the risk-difference estimate and its confidence interval provide more direct information about magnitude and uncertainty.

The registry does not provide a confidence interval for the sponsor’s chi-squared result, nor does it explain any difference in the calculation procedures. It is therefore not possible to determine from the record why the p-values differ. The safest interpretation is to retain both results with their methods clearly distinguished and to avoid inferring undocumented analytic choices.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists eleven outcome measures and ten posted secondary outcomes, alongside the primary outcome. When a study evaluates multiple outcomes, the chance of at least one apparently unusual result can increase if each is assessed separately without accounting for multiplicity. General statistical context: multiplicity procedures can control error rates across a defined family of tests, but the appropriate approach depends on the prespecified hierarchy and analysis plan. A multiplicity adjustment or hierarchy is not reported in the registry record.

The primary comparison is described as a chi-squared test. The record does not report whether the primary endpoint was designated before analyses began, whether secondary outcomes were formally confirmatory or exploratory, or whether any adjustment for multiple comparisons was planned. The posted primary result should therefore be interpreted on its own terms, without assuming that all outcomes were tested under a single prespecified framework.

The primary outcome description notes one participant inevaluable for analysis. The record does not explain why the participant was inevaluable, how the missing outcome was handled, or whether any sensitivity analysis was performed. The primary counts are 52 and 53, while the registry’s adverse-event denominators are 52 and 54. These are reported for different purposes, and the available information does not establish how the group totals relate across analysis populations. No reasons for the denominator differences should be inferred.

The registry does not report whether the primary analysis followed an intention-to-treat principle, whether participants were analyzed according to randomized assignment, or whether any participants were excluded after randomization beyond the inevaluable participant noted in the endpoint description. Details on imputation, missing-data assumptions, and sensitivity analyses are not reported in the registry record. These omissions limit assessment of how robust the result is to missing outcome information, but they do not by themselves show that the reported result is biased.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pancreatic leak (7.7%), gi other (5.8%), sepsis (3.8%), chyle leak (3.7%), abscess (3.7%).

The registry reports serious adverse events for 10 of 52 participants in the control arm and 10 of 54 in the experimental arm. Deaths are listed for 3 participants in each group. The other adverse-event counts are 39 of 52 in the control arm and 31 of 54 in the experimental arm. These are descriptive counts with the denominators recorded for safety reporting; they are not the primary efficacy analysis.

The serious adverse-event terms with the largest listed percentages include pancreatic leak at 7.7%, GI Other at 5.8%, sepsis at 3.8%, chyle leak at 3.7%, abscess at 3.7%, and BJ leak at 1.9%. The registry entries do not specify the group attribution of each listed term in the information, nor do they provide comparative statistical tests for adverse events.

These counts should not be interpreted as proving that the strategies have equal or different safety. The record does not provide event timing, severity details beyond the serious-event classification, causal attribution, or a formal comparative safety analysis. The safety denominators also differ from the primary-outcome denominators, so the counts should be read within their own reporting context.

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

The posted primary data show that 19 of 52 participants assigned to usual care and 27 of 53 assigned to the second-block strategy were discharged opioid-free. The unadjusted risk-difference estimate is 0.144 in the direction of a higher opioid-free proportion with the second block. However, the confidence interval crosses zero, and the registry’s chi-squared analysis reports p = 0.17. The result does not establish a clear difference between the strategies.

This finding should not be translated into a claim that the added block works or does not work. The trial’s estimate is uncertain, and the record does not report a threshold for what difference would be clinically important. A result that does not meet a conventional significance threshold does not prove equivalence, while a numerical difference by itself does not prove a treatment effect.

The endpoint is opioid-free status at discharge. It does not, on its own, summarize pain control, the amount of opioid used by participants who were not opioid-free, opioid use after discharge, or quality of life. Although these subjects appear among the listed secondary outcomes, their results are not included in the registry record for this analysis. No conclusions about those outcomes can be drawn from the primary result.

The trial compares two care strategies that both include a preoperative quadratus lumborum block and postoperative multimodal pain control; the experimental strategy adds a second block on day 4 after surgery. Accordingly, the primary result concerns the incremental comparison between those strategies, not the effect of a block versus no block. Interpretation is also limited by the missing detail about the original statistical plan, the single inevaluable participant, and the absence of reported missing-data methods.

17. Why This Trial Matters Statistically

This trial illustrates why reporting an effect estimate, an uncertainty interval, and a test result together is more informative than relying on a p-value alone. The raw group counts point toward a higher opioid-free discharge proportion in the second-block arm, and the risk difference gives an absolute-scale summary. The confidence interval nevertheless spans zero, showing that the estimated direction is not precise enough to settle whether the strategies differ.

It also demonstrates the value of defining the comparison carefully. Both groups received a preoperative quadratus lumborum block and multimodal pain care. The randomized contrast is the addition of a second block, so the result is relevant to that incremental decision rather than to regional anesthesia as a whole. Clear descriptions of the treatment contrast help prevent a broader interpretation than the trial supports.

Finally, the registry record exposes questions that statistical readers should ask even when a headline outcome and p-value are available. The original sample-size assumptions, missing-data approach, analysis population, multiplicity plan, and confidence interval for the sponsor’s test are not reported. The sample-size illustrations based on the observed effect can help readers understand planning scale, but they do not describe the trial’s original design or demonstrate that the trial had a particular probability of detecting its result.

These features matter because clinical interpretation depends not only on the direction of a point estimate, but also on its precision, the outcome definition, the analysis plan, and what the record leaves unknown. Here the central statistical message is a directionally favorable point estimate accompanied by substantial uncertainty.

18. Limitations

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

The primary comparison has limited precision: the risk-difference confidence interval includes zero and extends in both directions. The reported primary counts are 19 of 52 and 27 of 53, with one participant identified as inevaluable. The reason for inevaluability and the handling of that outcome are not reported in the registry record.

The registry does not report the original sample-size justification, the effect size used in its design, or the planned power. The sample-size illustrations based on the observed effect cannot fill that gap. Details of allocation concealment, the meaning and implementation of triple masking, and any interim analyses are also not reported in the registry record.

The posted primary analysis is a chi-squared test, but the record does not describe a prespecified analysis population, adjustment for baseline factors, or sensitivity analyses. It lists multiple secondary outcomes without reporting a multiplicity approach in the registry record for this result. The record also does not provide a sponsor-analysis confidence interval or explain the difference between the reported and recalculated p-values.

The primary outcome is specific to opioid-free status at discharge. The registry’s timeframe is listed as 90 days from surgery, but the endpoint description centers on discharge date; the record does not clarify this wording further. Secondary outcome results are not included in the primary analysis details, so interpretation cannot extend to the full set of opioid, cost, or quality-of-life outcomes.

Safety counts are available, but event timing, attribution, and formal comparisons are not reported. The adverse-event denominators differ from those used for the primary endpoint, and the record does not explain the difference. These limitations warrant a narrow reading of the result rather than assumptions about unreported procedures or outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Repeat Quadratus Lumborum Block to Reduce Opioid Need in Patients After Pancreatic Surgery — NCT03745794.
• Registry record last updated 2025-12-23; status last verified 2025-12.
• Results first posted 2023-02-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03745794 is a completed, randomized, parallel-group phase II trial sponsored by M.D. Anderson Cancer Center. It compared a preoperative quadratus lumborum block plus standard care with the same strategy plus a second block on day 4 after surgery. The primary endpoint was the number discharged opioid-free, with the comparison described as occurring on the discharge date and the timeframe listed as 90 days from surgery.

The primary counts were 19 of 52 in the control arm and 27 of 53 in the experimental arm. The recalculated unadjusted risk difference was 0.144, with a confidence interval crossing zero; the registry reports a chi-squared p-value of 0.17. The results do not establish a clear difference. Important details, including the original sample-size justification and missing-data methods, are not reported in the registry record.