Opioid Consumption and Disposal After Shoulder Arthroplasty: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Opioid Consumption and Disposal After Shoulder Arthroplasty (NCT05525975), a randomized na study. The primary outcome is Difference in Proportion of Participants With > 10 Pills Left Unused..

2. Clinical Question

The trial also recorded opioid disposal as a secondary outcome at 2-weeks or 6-weeks post-operative. These outcomes address different aspects of post-surgery medication use: the primary outcome concerns the number of unused pills, while the secondary outcome concerns disposal.

The registry record describes the study objective as developing and piloting preoperative opioid education and examining the effect of providing disposal mechanisms. The posted intervention description specifies educational materials, but the registry record does not describe a separate disposal mechanism as an intervention arm. The comparison in the posted results is education versus standard care.

3. Trial Design

The registry record describes a completed, randomized, single-blind, parallel-group trial. It lists enrollment of 140 and gives the study start as 2022-11-21 and primary completion as 2024-04-26. The record does not identify who was blinded, so the meaning of single-blind for participants, clinicians, or outcome assessors is not reported in the registry record.

The two arms were Control/Standard of Care and Education Arm. The control arm followed standard-care practices of the Shoulder Surgery Department at UIHC. The education arm received a brochure and watched an educational video at the preoperative work-up visit. The intervention description says the materials addressed opioid medications, pain management techniques, and proper disposal of excess opioid medication.

The trial included patients undergoing total shoulder replacement, described in the registry summary as anatomic total shoulder arthroplasty, reverse shoulder arthroplasty, and hemiarthroplasty. The primary outcome was assessed at 2 weeks or 6 weeks after surgery. The registry description says opioid use was self-reported on questionnaires completed during the first 2 weeks following surgery or at 6 weeks after surgery. The secondary disposal outcome has a timeframe of 2-weeks or 6-weeks post-operative.

The posted primary outcome arms include 63 participants in Control/Standard of Care and 64 in the Education Arm. The secondary outcome arms have their own reported denominators. The registry record does not explain the difference in outcome denominators, how participants were assigned to follow-up timepoints, or the details of randomization and allocation concealment. It also does not report the original design assumptions or a protocol-level statistical analysis plan.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Difference in Proportion of Participants With > 10 Pills Left Unused., measured over 2 weeks or 6 weeks after surgery.

The primary endpoint is the difference in the proportion of participants with more than 10 pills left unused. The registry labels the measure as a count of participants, but the comparison is a risk difference: the event is having more than 10 pills left unused, and each arm's count is interpreted relative to its reported denominator. The time frame is 2 weeks or 6 weeks after surgery.

The endpoint was intended to capture opioid consumption patterns after shoulder arthroplasty. The registry description says participants reported opioid use on questionnaires, the number of pills taken was documented, and research staff calculated morphine usage equivalents. The posted primary measure, however, is specifically the count of participants crossing the threshold for unused pills; it is not a direct estimate of average pills consumed.

A threshold outcome can make a group comparison easier to interpret in terms of whether participants had a specified amount left over. It also compresses information: participants just above and well above the threshold are counted in the same event category, while those below it are not. That is a general property of dichotomizing a measurement, not a finding about individual participants in this trial. The registry record does not report the distribution of unused pill counts or the rationale for selecting this threshold.

7. Results Posted in the Registry

• Education Arm: 73.4% (47/64) versus 77.8% (49/63) on control; risk difference -4.3 percentage points (95% CI -19.3 to 10.6), risk ratio 0.94 (0.77–1.15); unadjusted two-proportion z-test p = 0.569.

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.

Opioid Disposal

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Education Arm: 37.3% (22/59) versus 31.7% (19/60) on control; risk difference 5.6 percentage points (95% CI -11.4 to 22.7), risk ratio 1.18 (0.72–1.94); unadjusted two-proportion z-test p = 0.519.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Education Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome records opioid disposal, a behavior distinct from the primary measure of having more than 10 pills left unused. Its posted risk-difference estimate is positive for the Education Arm relative to standard care, while the primary estimate is negative for the Education Arm. The confidence intervals for both outcomes include zero, so the secondary pattern does not provide a clear, precise contrast that resolves the primary result.

These endpoints describe related but nonidentical parts of medication use. Having unused pills does not establish whether they were disposed of, and reporting disposal does not establish how many pills remained. The secondary outcome can therefore add descriptive context, but it should not be treated as another measurement of the same event or as confirmation of the primary endpoint.

The registry reports an unadjusted secondary p-value and no reported secondary analyses. The analysis methods and any prespecified hierarchy among outcomes are not reported in the registry record. When a study examines more than one outcome, unadjusted tests do not account for the increased opportunity for chance findings across comparisons. This general multiplicity concern means a secondary result usually carries less confirmatory weight unless its role and analysis plan were specified in advance.

The secondary endpoint also has different reported denominators from the primary endpoint. The record does not explain the difference, the reason for any unavailable observations, or how the analysis population was defined. Such details matter when interpreting whether the endpoint summaries represent the same participant set or follow-up pattern. The registry record does not report enough information to resolve those questions.

Overall, the secondary result should be read as an additional, uncertain description of disposal rather than as proof that the education materials changed disposal behavior. It neither establishes a secondary effect nor overturns the uncertainty in the primary comparison.

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

• Opioid Disposal

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared? The primary comparison is between the Education Arm and Control/Standard of Care for a binary event: having more than 10 pills left unused. A binary outcome places each participant into one of two categories for the analysis: the event occurred or it did not. The registry reports event counts and denominators for each arm, then gives a risk difference comparing the proportions.

A risk difference is an absolute contrast between proportions. A value below zero means the event proportion is lower in the intervention arm than in the control arm, according to the direction used for this comparison; a value above zero means it is higher. This is a general interpretation of the measure. It does not by itself establish a cause, explain why the groups differ, or indicate whether a difference matters clinically.

How should a confidence interval be read?

A confidence interval describes uncertainty around an estimated effect. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. The primary interval ranges from -0.193 to 0.106 and includes zero, the value corresponding to no risk difference. That means the posted data are compatible with effects on either side of zero under the interval method. The registry record does not identify the interval method or state whether the analysis was adjusted.

It is important not to interpret an interval as a range containing the true effect with a specific probability after the data have been observed. In the conventional frequentist interpretation, the confidence level describes the long-run performance of the procedure across repeated studies. The posted interval is useful as a measure of uncertainty, but its coverage depends on the method and assumptions used.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.569. In general, a p-value measures how unusual data at least as discordant with a null hypothesis would be if that hypothesis and the test assumptions held. It is not a measure of effect size, not the probability that chance alone produced the result, and not the probability that an intervention is effective. A p-value should be interpreted alongside the estimated difference and its confidence interval.

The registry record does not report the statistical test, model, or assumptions used for the posted comparison. The term “unadjusted” indicates that the displayed p-value is not adjusted for multiplicity in the posted results; it does not establish whether other covariate adjustments were made. Such adjustment details are not reported in the registry record.

Why report counts as well as proportions?

Counts show how many participants were recorded with the event, while denominators indicate the number represented in each arm's outcome summary. Proportions express those event counts relative to their arm denominators, allowing comparison when denominators differ. The registry gives both the counts and the risk-difference comparison. The outcome denominators are not identical across the primary and secondary results, and the record does not explain why they differ. It is therefore important to interpret each endpoint using its own reported arm summaries rather than treating the denominators as interchangeable.

The primary outcome is a threshold-based binary measure rather than a continuous count of unused pills. In general, turning a count into a binary event can simplify a comparison, but it discards variation within each category. It also makes the result dependent on the chosen cutoff. The registry record does not report the distribution of pill counts or explain the rationale for the more-than-10-pills threshold.

What can randomization support?

Randomization is a design approach intended to make assigned groups comparable, on average, with respect to both measured and unmeasured factors. That is a general rationale, not a guarantee that groups are balanced in a particular trial. The registry identifies the allocation as randomized but does not describe the sequence generation, concealment, or any checks of baseline comparability. The reported arm comparison should therefore be read as a comparison of the posted randomized groups, with implementation details not reported in the registry record.

The record describes the study as single-blind, but does not say who was blinded or whether blinding continued through outcome collection and analysis. Since the primary and secondary outcomes depend on participant reports, the details of outcome collection and the possible role of awareness are relevant, but cannot be assessed from the registry record.

What analyses are documented?

The registry posts arm-level counts and comparison estimates, but reports no analyses in its analysis listing. The exact inferential methods, analysis population, handling of missing observations, treatment of participants who did not follow the assigned approach, and any adjustment for baseline variables are not reported in the registry record. No conclusions about those choices should be inferred from the numerical summaries alone.

The secondary outcome is also binary, with opioid disposal recorded at 2-weeks or 6-weeks post-operative. Its risk difference and unadjusted p-value are posted, but no secondary analysis methods are described. In general, secondary outcomes may help characterize additional aspects of a trial, but when many outcomes or comparisons are considered, the chance of a chance finding can increase. The registry record does not report a multiplicity strategy, so the secondary result should not be treated as independently confirmatory.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.043, with a 95% confidence interval from -0.193 to 0.106. The interval extends across zero, which represents no difference on this scale, and allows for estimates in either direction. It is broad relative to the point estimate, so the posted comparison has limited precision. The data do not pin down a narrow range of plausible differences.

The point estimate alone can appear more definite than the evidence supports. The confidence interval shows that the observed results are compatible with a lower event proportion in the Education Arm, little or no difference, or a higher event proportion, under the interval method. The registry record does not state what magnitude of difference would be important, so statistical precision cannot be translated into a judgment about practical importance.

The secondary risk-difference interval also includes zero, ranging from -0.114 to 0.227 around an estimate of 0.056. This is likewise a broad interval. The outcome-specific denominators differ from those for the primary endpoint, and the registry record does not explain the reasons. Precision depends in part on how much information is available for each endpoint, as well as on the event frequencies and statistical method.

A confidence interval is not a guarantee that the true effect lies within its endpoints. In general, it summarizes uncertainty under a specified method and its assumptions. The registry record does not identify the interval calculation method, so its sensitivity to methodological choices cannot be assessed from the posted results alone.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations, not observed trial results. For these binary outcomes, the entries are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the participants per arm estimated to provide an 80% chance of detecting the specified effect if that effect is present and the planning assumptions hold. The 90% power column gives the corresponding estimate for a 90% chance. Power describes a design calculation for a planned study; it does not describe the probability that the posted result is correct.

Rows use 100%, 75%, and 50% of the observed effect as planning targets. Smaller effects require more participants per arm to detect under the same assumptions, which is why the planned counts increase as the effect fraction decreases. The planning estimates are based on the observed effect, so they should not be treated as independent estimates of the effect expected in a future study.

These figures are not observed power. The registry record does not report the trial's own original sample-size assumptions or justification. The posted enrollment and outcome denominators describe the completed study record, whereas the planning figures illustrate what a future design might require under the stated assumptions. They do not show that the study had a particular probability of detecting an effect after its results were known.

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 = 0.778; treatment proportion p₁ = 0.734; average p̄ = 0.756.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6073 = 1.1903.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6066 = 0.5105.
4. n = (1.1903 + 0.5105)² / (-0.0434)² = 1,535.6, rounded up to 1,536 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 <- 0.777777777777778                          # control proportion
p1 <- 0.734375                          # 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(5525975)
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 = 1,536 (80% power), 2,056 (90% power)
 75% of observed effect: n per arm = 2,690 (80% power), 3,600 (90% power)
 50% of observed effect: n per arm = 5,957 (80% power), 7,975 (90% power)
power.prop.test: 1535.6 
Simulated power at n = 1,536 per arm: 0.801 (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

The registry record does not report a statistical analysis plan describing how the primary and secondary outcomes were prioritized, whether additional outcomes were planned, or whether any multiplicity adjustment was intended. The primary endpoint is identified, and opioid disposal is listed as a secondary outcome, but no hierarchy for interpreting multiple results is given. The posted p-values are unadjusted.

Multiplicity matters because examining several outcomes or contrasts can increase the chance of observing at least one apparently unusual result even when there is no underlying effect. In general, prespecifying a primary endpoint and controlling how secondary findings are interpreted can help keep confirmatory claims aligned with the study question. Without a reported strategy, the secondary p-value should be treated cautiously. This does not change the numerical estimate; it affects how much evidential weight to place on it.

Missing-data handling is also not reported in the registry record. The posted primary and secondary summaries have different arm denominators, but the record does not explain whether that reflects missing questionnaires, different eligibility for the outcomes, different follow-up availability, or another reason. No imputation method, complete-case rule, or sensitivity analysis is described. The extent and potential influence of missing outcome data therefore cannot be assessed from the posted summaries.

The analysis population is not defined in the registry record. It is not stated whether the posted analyses followed an intention-to-treat approach, included only participants with observed outcomes, or used another population definition. The record also does not describe how participants who deviated from assigned treatment were handled. These are important features of randomized-trial analysis, but they cannot be inferred from arm labels or denominators.

Finally, the statistical test, model, and any adjustment for baseline factors are not reported. The posted estimates and unadjusted p-values can be described as recorded, but the absence of these methodological details limits independent assessment of assumptions and reproducibility. No claims about the handling of multiplicity, missingness, or analysis populations are warranted beyond what the registry record states.

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 0% reporting threshold.

The registry's safety summaries list 0 serious adverse events and 0 other adverse events for Control/Standard of Care, with 63 at risk in each category. For the Education Arm, the summaries list 0 serious adverse events and 0 other adverse events, with 64 at risk in each category. The registry lists 0 deaths in each arm.

These figures should be read as the values recorded in the registry's safety fields. They do not describe the type, severity, timing, or relatedness of individual events, and no serious adverse event terms are listed. The registry record does not provide further detail about safety-event collection, definitions, or follow-up procedures. The figures therefore do not establish that no events occurred outside the reported fields or capture every aspect of safety experience.

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

The posted results estimate the difference between the Education Arm and standard care in the proportion of participants with more than 10 pills left unused after shoulder arthroplasty. The primary estimate is -0.043, and the confidence interval includes zero while allowing differences in either direction. The result is therefore uncertain: it does not identify a precise group difference, and it does not establish that the groups are equivalent.

The secondary opioid-disposal estimate is also uncertain, with a confidence interval that includes zero. It concerns a different outcome and has an unadjusted p-value. Neither the primary nor secondary numerical summary should be interpreted in isolation from its uncertainty, outcome definition, and the registry's limited reporting of analysis methods.

These findings do not establish that the education intervention causes a change in opioid use, unused pills, or disposal. Randomization is a design feature intended to support causal comparisons, but evaluating that support also requires information about implementation, follow-up, missing outcomes, and analysis populations. The registry record does not report several of those details.

The results also do not show that participants used a particular number of pills on average. The primary endpoint is a threshold count of participants, not a mean consumption measure. Nor do the posted results establish why any pills remained unused or whether disposal occurred for those pills. The record does not report the distribution of individual pill counts or detailed disposal outcomes.

Statistical uncertainty is not the same as evidence that an intervention has no effect. The interval includes both negative and positive risk differences, and the registry record does not specify a threshold for a meaningful effect. The appropriate reading is a cautious description of the posted estimates, not a treatment recommendation or a definitive conclusion about benefit, harm, or equivalence.

17. Why This Trial Matters Statistically

This trial addresses a practical measurement challenge: opioid use after shoulder arthroplasty and the handling of medication left over after surgery. The registry describes education about opioid medications, pain management, and disposal, while the outcomes distinguish unused pills from reported disposal. Statistically, that distinction matters because related behaviors are not interchangeable endpoints.

The primary outcome converts pill use into a threshold-based event. This makes the comparison a difference in proportions, which is straightforward to describe, but it also discards information about variation within the event and non-event categories. The registry does not report the underlying distribution of pills, so readers cannot assess how the threshold relates to the range of reported consumption.

The trial also illustrates why effect estimates need uncertainty intervals. The primary point estimate is not enough to characterize the evidence: its interval includes zero and extends across differences in either direction. The secondary estimate is uncertain as well. The direction of a point estimate alone should not be confused with a precise or definitive finding.

Finally, registry transparency affects interpretation. The record identifies the design, arms, outcome definitions, and posted summaries, but does not report key details such as the analysis plan, handling of missing outcomes, or multiplicity strategy. These omissions do not erase the posted results, but they limit how fully readers can evaluate the methods behind them. That distinction—between describing available estimates and making stronger claims—is central to careful clinical-trial interpretation.

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.

Several limitations specific to this trial are visible in the registry record. The primary outcome relies on self-reported opioid use collected by questionnaire, according to the outcome description. The record does not report how self-reports were verified, how pill counts were captured, or how the threshold of more than 10 pills left unused was selected. The posted endpoint is therefore narrower than a full description of consumption or leftover medication.

The primary outcome allows assessment at 2 weeks or 6 weeks after surgery, while the description also refers to questionnaires during the first 2 weeks following surgery or at 6 weeks. The record does not clarify how participants were assigned to or grouped by follow-up time, whether timing differed by participant, or how timing was handled in the comparison. The secondary outcome likewise gives a 2-weeks or 6-weeks post-operative timeframe without further detail.

The arm denominators differ between the primary and secondary outcome summaries. The registry record does not explain why, identify whether observations were missing, or describe the analysis population. Consequently, the effect of incomplete follow-up or outcome availability cannot be assessed from the record.

The record describes the study as single-blind but does not identify who was blinded. It does not report details of randomization procedures, allocation concealment, baseline comparability, or adherence to the educational intervention. Statistical methods, multiplicity handling, and the original sample-size justification are also not reported in the registry record.

These reporting gaps constrain interpretation of the posted estimates. They do not demonstrate that a particular problem occurred; they mean that readers cannot determine from the registry record whether or how these issues affected the comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Opioid Consumption and Disposal After Shoulder Arthroplasty — NCT05525975.
• Registry record last updated 2026-01-15; status last verified 2026-01.
• Results first posted 2025-03-27.
• 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

NCT05525975, titled “Opioid Consumption and Disposal After Shoulder Arthroplasty,” is listed as a completed, randomized, single-blind, parallel-group trial. The registry record lists enrollment of 140 and study dates from 2022-11-21 to primary completion on 2024-04-26.

The comparison is preoperative educational materials versus standard care for participants undergoing shoulder arthroplasty. The primary outcome is the difference in the proportion with more than 10 pills left unused at 2 weeks or 6 weeks after surgery. The posted estimate is -0.043, with a 95% confidence interval from -0.193 to 0.106 and an unadjusted p-value of 0.569.

Opioid disposal is listed as a secondary outcome. Its posted estimate is uncertain, and the registry record does not report an analysis plan, missing-data methods, or a multiplicity strategy. The results are best understood as imprecise comparisons of the recorded outcomes, with important methodological details not reported in the registry record.