Efficacy of EUS-guided Celiac Plexus Blockade in Chronic Pancreatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of EUS-guided Celiac Plexus Blockade in Chronic Pancreatitis (NCT00658736), a randomized phase 3 study. The primary outcome is Change in Pain Disability Index.

2. Clinical Question

In statistical terms, the trial asks whether adding triamcinolone to the bupivicaine block is associated with a different chance of meeting the registry’s threshold for meaningful improvement in pain-related limits on daily activities. The endpoint is a binary classification: each participant either met the stated threshold or did not. That makes the primary result a comparison of event proportions rather than a comparison of average PDI scores.

The registry record describes a randomized, parallel-group trial and identifies the intervention and comparator as drug interventions. It does not report further detail about the eligible population, such as disease duration, prior treatment, or criteria for pain severity. Those omissions limit how specifically the result can be related to particular patient groups. The record also does not report a separate statistical analysis plan or a fuller description of the primary endpoint’s analysis population.

3. Trial Design

This was a randomized, parallel-group phase 3 trial sponsored by The Cleveland Clinic. The registry lists an enrollment of 40 and a completed status. The recorded start was 2008-03, and the primary completion date was 2011-01. The two groups received the same type of endoscopic ultrasound-guided celiac plexus blockade, with the distinguishing feature being whether triamcinolone was included alongside bupivicaine.

The combination group had 21 participants in the posted primary outcome results, and the bupivicaine-alone group had 19. The arm descriptions specify the same 20 cc injectate volume and the same EUS-guided procedure for both groups. This shared procedural approach makes the added corticosteroid the principal treatment contrast described in the registry record. Further procedural details, including how treatment delivery was standardized or whether rescue treatment was permitted, are not reported in the registry record.

The brief summary calls the trial triple-blind, while the registry’s masking classification is quadruple. The record does not clarify how those descriptions relate to each other or identify which roles were masked. It therefore supports describing the trial as masked, but not a more detailed account of masking procedures. The official title also calls it triple-blinded.

The registry identifies the primary outcome as a count of participants with a qualifying decrease in Pain Disability Index score at 1 month after the block. It lists a secondary outcome measuring change from baseline in the SF12 Physical Component at 1 month. Original sample-size assumptions, the planned statistical analysis, handling of missing outcome data, and analysis-population definitions are not reported in the registry record. The trial’s randomized design is relevant to interpreting the treatment contrast, but the posted information does not establish every detail needed to assess implementation or analysis choices.

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 Change in Pain Disability Index, measured over 1 month after block.

The primary endpoint is a count of participants with a decrease of at least 10 points in the Pain Disability Index at 1 month after the block. The PDI measures how much pain limits a person’s ability to carry out everyday tasks. Its scale runs from 0, indicating no limitation, to 70, indicating severe limitation. Under the registry’s endpoint description, a decrease of 10 points or more is considered significant improvement in the ability to carry out daily activities.

Using a threshold turns a score change into a binary outcome. Each participant is classified according to whether the decrease met the specified cutoff. The resulting group comparison concerns the proportion of participants who crossed that cutoff, rather than how far scores changed on average or how many participants experienced smaller changes. This can make the endpoint easy to interpret as a participant count, but it also means that changes close to the threshold may be classified differently even when their underlying score changes are similar.

The PDI is used because the trial concerns pain-related disability, not pain intensity alone. A disability measure focuses on the extent to which pain affects everyday activity. The registry record does not report whether the threshold was selected specifically for this trial, nor does it provide additional details about the timing or method of PDI assessment beyond the stated 1-month timeframe. The posted primary outcome therefore supports interpretation of the reported responder counts against the stated threshold, while leaving those design details unreported.

7. Results Posted in the Registry

• Bupivicaine Alone: 15.8% (3/19) versus 14.3% (3/21) on control; risk difference 1.5 percentage points (95% CI -20.7 to 23.7), risk ratio 1.11 (0.25–4.83); unadjusted two-proportion z-test p = 0.894.

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.

Change From Baseline in Quality of Life Score at 1 Month - SF12 Physical Component

• 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:
  • Bupivicaine Alone: mean 1.70 versus -0.20 on control; difference 1.90 (95% CI -3.19 to 6.99), standardized effect d = 0.23; z-test p = 0.465.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupivicaine Alone and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome, change from baseline in the SF12 Physical Component at 1 month. Taken together, the primary and secondary results do not provide a consistent, precise indication of separation between the groups: both comparisons are uncertain, and neither interval excludes no difference. The outcomes address related but distinct concepts. The primary result concerns a threshold for pain-related disability, whereas the secondary measure concerns a physical component of quality of life.

The secondary outcome can provide context alongside the primary endpoint, but it does not validate or replace the primary result. A quality-of-life measure may capture aspects of a participant’s experience that are not represented by a disability threshold, and the reverse is also true. The registry record does not report a prespecified hierarchy or a confirmatory role for the secondary endpoint. The secondary findings should therefore be viewed as additional descriptive information rather than an independent confirmation of the primary comparison.

Unadjusted secondary results carry less weight when several outcomes or analyses may be considered, because the chance of finding an apparently notable result can increase as more comparisons are made. This is the general statistical issue of multiplicity. The registry record does not report a multiplicity adjustment or a plan for controlling the interpretation of multiple outcomes. It also lists no reported analyses for the secondary outcome. Consequently, the posted secondary comparison should be treated cautiously and not used alone to make a strong claim about a treatment difference.

The overall pattern is best read as limited evidence across the registered outcomes, rather than as a set of independent tests that settle the treatment question. The registry does not report additional secondary outcomes or analyses that would support broader conclusions.

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

• Change From Baseline in Quality of Life Score at 1 Month - SF12 Physical Component

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary outcome, the reported endpoint is binary: participants either had a decrease of at least 10 PDI points or did not. A comparison of two such groups can be expressed as an absolute risk difference, a risk ratio, or an odds ratio. These measures describe different scales of the same underlying event comparison. The posted recalculation uses the risk difference as its main contrast, with bupivicaine alone compared with bupivicaine and triamcinolone. An absolute risk difference is the difference between the event proportions in the two groups; a value of zero represents no difference on that scale.

The registry reports 3 qualifying participants in each group, with 21 participants in the combination group and 19 in the bupivicaine-alone group. The calculated event proportions are 0.143 and 0.158, respectively. The estimated risk difference is 0.015. These estimates are unadjusted: they compare the posted group summaries without adjustment for other variables. The registry does not report a sponsor-conducted analysis for this primary comparison, and the posted analysis count is 0. The recalculated comparison should therefore be understood as a simple summary-statistic analysis rather than a fully documented trial analysis.

A p-value measures how surprising a result at least as far from the null as the observed result would be under the null model and its assumptions. It does not give the probability that the null hypothesis is true, and it is not a measure of clinical importance. The unadjusted p-value for the primary comparison is 0.894. That value does not establish equivalence or rule out potentially meaningful differences. It indicates that the observed contrast is not unusual under a model assuming no difference, while the confidence interval gives a more direct view of the range of effect sizes compatible with the data.

Confidence intervals describe uncertainty around an estimate. A narrow interval indicates more precision than a wide interval, conditional on the method and assumptions used. The primary risk-difference interval extends from -0.207 to 0.237, including zero and values in either direction. The registry record does not report the confidence level or the exact method used for this recalculation. The interval should accordingly be read as the posted uncertainty range, without assigning an unreported method or confidence level.

For the secondary SF12 Physical Component outcome, the registry reports mean change from baseline and standard deviation by group. A mean difference compares the average changes, while the standard deviations describe the spread of participant-level changes within each group. The recalculated mean difference is unadjusted. The registry does not report a secondary-outcome analysis, so the result does not include evidence of adjustment for baseline variables or other covariates.

When outcomes are continuous, the mean summarizes the central tendency, but it does not show the full distribution of individual responses. Standard deviations indicate variability around the group means; they are not confidence intervals for the mean. A confidence interval for a mean difference combines the estimate with its sampling uncertainty. The secondary comparison’s interval spans negative and positive values, so the posted summary statistics do not precisely establish a direction for the group contrast.

Why does over-dispersion matter?

Over-dispersion is a general concern when observed variability is greater than a statistical model expects. If a model assumes less variability than the data contain, its uncertainty estimates can be too small and its intervals too narrow. Conversely, a model that accounts for extra variability can give more cautious uncertainty estimates. This is a general statistical consideration, not a reported feature of this trial. The registry record does not describe a model for over-dispersion, and the simple binary comparison does not report a dispersion parameter.

What can be inferred from randomization?

In general, random allocation is intended to make treatment groups comparable with respect to measured and unmeasured characteristics at assignment, apart from chance variation. That goal helps support causal interpretation when allocation is implemented as planned and follow-up and analysis are handled appropriately. Randomization does not guarantee exact balance, particularly in a small trial, and does not resolve missing-data or adherence issues. The registry identifies randomized allocation but does not report allocation concealment, sequence generation, adherence, or analysis-population details.

Why distinguish the trial analysis from recalculation?

A trial’s planned analysis can include a prespecified endpoint definition, model, covariate adjustment, handling of missing observations, and population for analysis. A recalculation from summary counts or means cannot recover those choices when they are not reported. Here, the registry reports no analyses for the listed outcomes, and the record does not give the original statistical plan. The unadjusted calculations are useful for describing the posted summaries and their uncertainty, but they should not be presented as the trial’s documented primary analysis.

Planning calculations use a different purpose from outcome analysis. The sample-size illustrations estimate how many participants per arm would be required under stated assumptions to detect a fraction of the observed effect at specified power levels. They do not measure the probability that this completed trial detected an effect. Power is a design quantity defined for a specified effect and set of assumptions; it cannot be reconstructed as an observed property of a trial simply by inserting the result into a formula.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.015, with a confidence interval from -0.207 to 0.237. The interval crosses zero, the value representing no difference on the risk-difference scale. It also extends in both directions, so the posted result is compatible with a lower event proportion in the bupivicaine-alone group or a higher one. The point estimate alone should not be treated as a precise estimate of the underlying contrast.

In general, a confidence interval gives a range of estimates compatible with the data and the calculation method, conditional on its assumptions. Its width conveys precision: wider intervals leave more uncertainty about the magnitude and direction of an effect. The primary interval is broad relative to the point estimate, reflecting limited information in the posted event counts. The registry record does not report the confidence level or calculation method for this recalculated interval, so those details should not be inferred.

The secondary mean-difference interval is -3.194 to 6.994. It too includes zero and covers values in both directions. This indicates uncertainty about the direction and magnitude of the average-change contrast. It does not establish that the groups are identical, nor does it show that every value in the interval is equally plausible.

Intervals do not account automatically for every limitation in a registry record. They cannot address unreported missing-data procedures, selective outcome reporting, or uncertainty about the planned analysis. The posted intervals quantify sampling uncertainty under their calculation assumptions; broader uncertainty about trial conduct and analysis remains relevant.

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 illustrations are planning calculations, not a reconstruction of the trial’s original design. The original sample-size assumptions and justification are not reported in the registry record. The stated illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers detecting 100%, 75%, or 50% of that effect.

For these outcomes, the figures are participants per arm, not total participants across the trial. The note about total events applies to time-to-event calculations, and the posted outcomes are not time-to-event outcomes. For example, the primary-outcome illustration gives participants per arm for 80% power and participants per arm for 90% power under each stated effect fraction. The 80% column describes a design targeting an 80% chance of detecting the specified effect under the assumptions; the 90% column describes a higher target chance for that same specified effect. Higher target power generally requires more participants.

Each effect fraction asks about a smaller difference than the preceding, larger-effect scenario. Detecting a smaller effect generally requires more participants, because a small contrast is harder to distinguish from random variation. The posted estimates therefore illustrate how planning requirements rise as the target effect becomes more modest. They are not observed power: observed power is not a meaningful substitute for reading the estimated effect and its confidence interval after a trial is complete.

The plotted sample-size relationship should be read as a visual expression of those planning assumptions, not as additional trial evidence. Its estimates depend on the observed effect used as the starting point, which itself is uncertain. The registry record does not say that these illustrations were used to plan this trial, and they should not be interpreted as the trial’s intended enrollment target.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.143; treatment proportion p₁ = 0.158; average p̄ = 0.150.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5055 = 0.9908.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5054 = 0.4253.
4. n = (0.9908 + 0.4253)² / (0.0150)² = 8,868.1, rounded up to 8,869 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 <- 0.142857142857143                          # control proportion
p1 <- 0.157894736842105                          # 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(658736)
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 = 8,869 (80% power), 11,872 (90% power)
 75% of observed effect: n per arm = 15,604 (80% power), 20,889 (90% power)
 50% of observed effect: n per arm = 34,742 (80% power), 46,510 (90% power)
power.prop.test: 8868.1 
Simulated power at n = 8,869 per arm: 0.798 (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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators examine several outcomes, time points, subgroups, or analysis choices. In general, repeated testing can increase the chance of at least one apparently unusual result even when no underlying differences exist. A prespecified hierarchy or adjustment procedure can help define how multiple findings should be interpreted. The registry record does not report a multiplicity plan or identify any adjustment for testing more than one outcome.

The record lists a primary PDI endpoint and one secondary SF12 Physical Component endpoint. It does not report whether there were additional outcomes that were collected but not posted, whether other time points were assessed, or whether subgroup analyses were planned. No conclusion about unreported analyses can be drawn from the absence of those details. The listed outcomes should be interpreted according to their stated roles, while recognizing that the handling of multiple comparisons is not described.

Missing-data methods are also not reported in the registry record. The posted arm counts show the number of participants used for the outcome summaries, but the record does not explain whether those counts include everyone randomized, how missing measurements were handled, or whether any participants were excluded from analysis. It does not describe imputation, sensitivity analyses, or reasons for missing outcomes. These omissions matter because the interpretation of an outcome comparison can depend on which participants contribute data and why other measurements are absent.

The analysis populations are not reported in the registry record. Although allocation was randomized, the record does not say whether the results follow an intention-to-treat approach, a per-protocol approach, or another definition. It also does not report protocol deviations, treatment adherence, or loss to follow-up. Without these details, the reported counts and summary statistics can be described, but the precise relationship between those summaries and the randomized groups is not fully documented.

These gaps do not by themselves show that the analyses were inappropriate. They limit what can be verified from the registry record and make it important to distinguish the posted unadjusted recalculations from a fully documented analysis plan.

15. 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 non-serious adverse event terms

The registry reports serious adverse events for 0 of 21 participants in the bupivicaine-and-triamcinolone group and 0 of 19 participants in the bupivicaine-alone group. These figures mean that no serious adverse events were recorded in either group in the posted results. They do not establish that the risk of serious events is absent; an event not observed in a trial of this size may still be possible.

Other adverse events were reported for 4 of 21 participants in the combination group and 2 of 19 participants in the bupivicaine-alone group. The registry does not provide further detail about the nature, severity, timing, or relatedness of those other events in the posted figures. Death counts are not reported in the registry record.

Safety counts should be interpreted alongside the period and completeness of adverse-event collection, which are not specified in the available record. They describe what was recorded in these trial groups and do not provide a complete estimate of uncommon or longer-term events.

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

The primary result describes the proportion of participants meeting a specified PDI improvement threshold at 1 month after the block. The posted counts are similar in the two groups, and the recalculated estimate is close to no difference. However, the confidence interval is broad and includes contrasts in both directions. The result therefore does not provide a precise estimate of the difference between the groups.

A non-significant p-value does not prove that the treatments are the same. Showing equivalence or non-inferiority requires a design and analysis with a prespecified margin and appropriate inference; the registry record does not report such a framework. Likewise, the posted results do not establish that either intervention is effective or ineffective. They describe the observed outcome counts and the uncertainty around an unadjusted comparison.

The endpoint is specific: it counts participants whose PDI score decreased by at least 10 points. It does not capture every possible change in pain, function, quality of life, or treatment experience. The result applies to the stated threshold and timeframe and cannot be assumed to describe other outcomes or follow-up periods. The record gives one secondary quality-of-life measure, but it does not report a broader set of confirmatory analyses.

The trial was randomized, which is a useful design feature for comparing assigned groups. Still, the registry record does not describe allocation procedures in detail, masking roles, missing-data handling, adherence, or analysis populations. Those unreported elements limit the assessment of how the randomized comparison was implemented and analyzed.

The most defensible statistical reading is that the posted data do not sharply distinguish the groups on the registered primary endpoint. They leave substantial uncertainty about the size and direction of any difference. This is a statement about the information in the recorded outcome data, not a recommendation about treatment choice.

17. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty, and the study design need to be considered together. The observed primary counts are easy to state, but the confidence interval shows that the comparison is not precise enough to settle the direction or magnitude of a difference. A p-value alone would not convey that range of uncertainty.

It also illustrates the distinction between a binary responder endpoint and a continuous measure. The primary outcome classifies participants by whether their PDI decrease reached a specified threshold. The secondary outcome summarizes average change on a quality-of-life scale. These approaches answer different questions, and one cannot be treated as a direct substitute for the other. A threshold can aid interpretability, but it does not preserve all information about the amount of change in each participant.

The record also shows why registry transparency matters. Key features needed to evaluate a statistical analysis—such as the original sample-size justification, missing-data procedures, multiplicity plan, and analysis-population definition—are not reported. Their absence does not establish poor conduct, but it limits independent assessment of whether the posted comparisons match the planned analyses.

Finally, planning calculations based on an observed effect should not be confused with evidence about what the completed trial had a probability of detecting. The illustrations can clarify how target effect size and power relate to participant requirements, while remaining separate from the trial’s own unreported design assumptions. Keeping those distinctions clear prevents a limited, imprecise result from being overstated.

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 main trial-specific limitation is the modest number of participants contributing to the posted results: 21 in the combination group and 19 in the bupivicaine-alone group. The primary endpoint events are also few, with 3 participants meeting the threshold in each group. These counts leave substantial uncertainty in the comparison, as reflected by the broad confidence interval.

Follow-up for the primary endpoint is stated as 1 month after the block, and the secondary quality-of-life outcome is also at 1 month. The registry record does not report longer-term outcome results. The posted findings therefore do not describe whether the outcomes changed beyond that timeframe. The record also does not report baseline PDI summaries or individual change distributions, limiting assessment of the score-level pattern behind the responder counts.

The masking descriptions are not fully reconciled: the brief summary and official title call the trial triple-blind, while the registry classification says quadruple masking. The record does not explain which groups of people were masked. It also does not report allocation-concealment procedures, adherence, protocol deviations, missing-data methods, or the analysis population.

The analysis details are limited. No primary or secondary analyses are reported in the registry, and the available comparisons are unadjusted recalculations from posted summaries. The original sample-size justification, statistical plan, and multiplicity strategy are not reported. The registry lists one secondary outcome, which provides only a narrow view of other possible dimensions of pain and function.

The record identifies The Cleveland Clinic as sponsor, but the number of study sites is not reported. Further eligibility criteria and details needed to assess how closely the enrolled population matches other groups are also not reported in the registry record. These limits narrow both the statistical assessment and the scope of conclusions that can be drawn from the posted data.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy of EUS-guided Celiac Plexus Blockade in Chronic Pancreatitis — NCT00658736.
• Registry record last updated 2017-06-14; status last verified 2017-05.
• Results first posted 2017-06-14.
• 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

NCT00658736 is a completed randomized, parallel-group phase 3 trial sponsored by The Cleveland Clinic. It enrolled 40 participants and compared EUS-guided celiac plexus blockade with bupivicaine and triamcinolone against the same procedure with bupivicaine alone. The registry records a start date of 2008-03 and a primary completion date of 2011-01.

The primary outcome counted participants with a decrease of at least 10 points on the Pain Disability Index at 1 month after the block. Three participants in each group met that threshold. The recalculated unadjusted risk difference is 0.015, with a confidence interval from -0.207 to 0.237 and an unadjusted p-value of 0.894. The record also lists change in the SF12 Physical Component at 1 month as a secondary outcome.

The registry does not report the original sample-size justification, statistical analysis plan, missing-data methods, multiplicity plan, or analysis populations. The posted comparison is therefore best read as an unadjusted description of the recorded summaries and their uncertainty.