PRescribing INterventions for Chronic Pain Via the Electronic Health Record Study - Current Opioid-User Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PRescribing INterventions for Chronic Pain Via the Electronic Health Record Study - Current Opioid-User Population (NCT04601480), a randomized na study. The primary outcome is Opioid Tapering Rate, Category 1.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with four clinic assignments: Care as Usual, Choice Architecture Nudge, PMP Integration & Nudge, and Choice Architecture Nudge + PMP Integration & Nudge. The registry describes clinics as assigned to these care approaches. It lists the study as single-masked, but which people were masked and how masking was maintained are not reported in the registry record.

The study objective was to assess whether electronic health record (EHR)-based decision-support tools affected primary care provider decision-making around pain treatment and opioid prescribing. The tools were informed by behavioral economics and were intended to nudge, but not compel, clinicians toward guideline-concordant care. The design includes the two individual approaches and their combination, with usual care as the comparator.

The registry reports an enrollment of 309. The primary outcome results list arm counts of 74 for Care as Usual, 62 for Choice Architecture Nudge, 70 for PMP Integration & Nudge, and 77 for the combined intervention. The meaning of the difference between the enrollment figure and the arm counts used for the primary outcome is not reported in the registry record; participant flow and the analysis population are not described in the posted material.

The study began on 2020-08-26, reached primary completion on 2021-10-01, and is listed as completed. The primary outcome timeframe is 12 months. The registry also lists Prescription Reduction vs Discontinuation Rate as a secondary outcome. Details of the protocol, recruitment, clinic count, and intervention delivery are 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: The original study protocol included a potential second randomization period after six months into the trial. This secondary randomization did not occur, per the recommendation of the Data Monitoring Committee.

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.

Population: Data was not collected on age or race

6. Primary Endpoint

The registry lists the primary outcome as Opioid Tapering Rate, Category 1, measured over 12 months.

The primary endpoint is Opioid Tapering Rate, Category 1, reported as the mean proportion of opioid-refill-eligible visits per PCP that met the definition of an appropriate taper during 12 months. The relevant visit involved someone currently receiving a high-risk opioid. A visit counted in Category 1 when an order reduced MME by no greater than 20% relative to the current prescription and there was documented evidence that the reduction was consistent with CDC guidelines.

This endpoint focuses on prescribing decisions and their documentation. It distinguishes a guideline-consistent, limited MME reduction from a reduction without supporting documentation or one exceeding the stated threshold, and from a visit with no MME reduction. The primary result concerns Category 1 only. It does not by itself report the frequency of the other categories, the total number of individual patients who experienced a taper, or any patient health outcome.

Using a proportion of eligible visits per PCP allows the outcome to represent the share of relevant prescribing opportunities that fell into the defined category. The registry reports a mean and standard deviation for this continuous measure. General statistical context: an endpoint defined at the visit or provider level may capture prescribing practice, but interpretation depends on how visits and providers were selected and analyzed. Those operational and analysis details are not reported in the registry record.

7. Results Posted in the Registry

• Choice Architecture Nudge: mean 0.04 versus 0.02 on control; difference 0.02 (95% CI -0.04 to 0.07), standardized effect d = 0.10; z-test p = 0.561.
• PMP Integration & Nudge: mean 0.03 versus 0.02 on control; difference 0.01 (95% CI -0.04 to 0.06), standardized effect d = 0.05; z-test p = 0.765.
• Choice Architecture Nudge + PMP Integration & Nudge: mean 0.02 versus 0.02 on control; difference -0.00 (95% CI -0.04 to 0.04), standardized effect d = -0.00; z-test p = 0.996.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is described as a continuous measure summarized by its mean and standard deviation. Each value represents the proportion of opioid-refill-eligible visits per PCP that fell into Category 1, appropriate tapering. The registry reports one mean and standard deviation for each trial arm. General statistical context: a mean gives the average value in a group, while a standard deviation describes how dispersed individual observations are around that average. Here, the relatively large standard deviations indicate that the average should not be taken to mean that the observed proportions were similar across all providers.

What does a mean difference represent?

For each intervention, the posted comparison expresses its arm mean minus the Care as Usual mean. The Choice Architecture Nudge estimate is 0.017; the PMP Integration & Nudge estimate is 0.007; and the combined-approach estimate is -< 0.001. A positive estimate means the intervention arm's posted mean was higher than the comparator mean, while a negative estimate means it was lower. These estimates are expressed on the outcome's proportion scale. They are not adjusted for other variables in the results presented.

General statistical context: an unadjusted comparison uses the observed group summaries without accounting for other measured factors or design features in a regression or other adjustment model. Random assignment is part of this trial's design, but interpretation of clinic-assigned interventions may also depend on the analysis unit and on the relationship among observations within clinics and providers. The registry does not report whether or how such dependence was handled. It also does not report a model specification, standard-error method, or adjustment covariates.

How should the confidence intervals be read?

A confidence interval describes the range of values reasonably compatible with the observed estimate under the statistical method used. General statistical context: a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the effect size. The intervals reported for the three comparisons all cross zero. In this setting, zero represents no mean difference between an intervention and Care as Usual. The intervals therefore do not rule out either a decrease or an increase in the mean proportion, and they include zero difference.

The registry's comparison results give unadjusted p-values of 0.561, 0.765, and 0.996, respectively. General statistical context: a p-value measures how unusual data at least as extreme as those observed would be under a specified no-difference model, assuming the analysis conditions hold. It does not give the probability that the no-difference model is true, and it is not a measure of clinical importance. The posted p-values should be considered alongside the effect estimates, confidence intervals, and limitations of the reported analysis. The registry does not report an adjustment for the multiple intervention comparisons.

Why can variability matter for a proportion outcome?

The outcome is based on a provider-level proportion, but the underlying number of eligible visits for each PCP is not reported. General statistical context: proportions based on different numbers of opportunities can have different precision. A proportion based on few eligible visits may be more variable than one based on many visits. Without visit denominators, provider-level distributions, or the analysis method, it is difficult to determine how much each PCP's proportion contributes to an arm mean or how well the standard errors reflect differing denominators.

General statistical context: over-dispersion occurs when variability is greater than expected under a simple model for the data. It matters because standard errors and confidence intervals can be too optimistic if a model assumes less variability or independence where observations are correlated. In this trial, observations may be organized by PCP and clinic, and assignment is described at the clinic level. The registry does not report a clustering adjustment or other model details. That absence does not show that clustering was ignored; it means the approach is not reported and cannot be evaluated from this record.

The posted summaries are useful for describing the arm means and the unadjusted differences, but they do not provide a complete account of the statistical analysis. The registry does not report missing-data handling, definitions of the analysis population, a prespecified analysis plan, or whether interim analyses were planned or performed.

10. Confidence Intervals and Precision

The estimated mean differences are imprecise enough that each confidence interval includes both zero and values on either side. For Choice Architecture Nudge, the estimate is 0.017, with a 95% confidence interval from -0.039 to 0.073. For PMP Integration & Nudge, it is 0.007, with a 95% confidence interval from -0.042 to 0.057. For the combined approach, it is -< 0.001, with a 95% confidence interval from -0.044 to 0.044.

General statistical context: a confidence interval communicates uncertainty around an estimate rather than a guaranteed range for the true effect. If a method is well calibrated under its assumptions, intervals constructed in the same way across repeated studies would cover the target effect at the stated rate. The registry record does not describe the method used to construct these intervals, so readers cannot assess its assumptions or whether it accounted for clinic or provider clustering.

Since each interval crosses zero, the posted results do not distinguish a difference from no difference using these intervals alone. The ranges also permit effects in opposing directions, so the observed point estimates should not be treated as precise estimates of the direction or magnitude of an intervention effect. The standard deviations—0.138, 0.186, 0.161, and 0.137 across the four arms—also show considerable spread in the provider-level proportion measure relative to the arm means.

The arm counts reported with the endpoint are 74, 62, 70, and 77. The number of eligible visits contributing to each provider's proportion, the number of providers or clinics, and any exclusions are not reported in the registry record. Those details would help readers understand the sources of uncertainty and the effective amount of information in the comparisons.

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 sample-size figures are planning illustrations based on the observed comparison effects, not the trial's original design calculations. They are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes across both arms and are not total event counts. The registry record's assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

In plain language, the 80% power column gives the participants per arm estimated to be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect is real. The 90% power column gives the corresponding per-arm number for a 90% chance. These are hypothetical planning quantities, not evidence about the achieved power of this trial. The sample-size calculations are not observed power.

The planning illustrations include effects set at 100%, 75%, and 50% of the observed effect for each comparison. Smaller effects require more participants to distinguish them from random variation under the same assumptions. The figures become especially large for the combined approach because its observed mean difference is very close to zero; the illustration based on that estimate is therefore not a practical forecast of the size of a future study.

These calculations do not account for unreported design features such as clinic-level assignment or within-clinic dependence. The registry's original sample-size rationale and original design assumptions are not reported in the registry record. The illustrations should therefore be read as conditional planning examples based on the posted effect estimates, not as a reconstruction of the completed trial's design or a recommendation for a future trial.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.017; pooled standard deviation σ = 0.162.
2. n = 2 × (1.96 + 0.842)² × 0.162² / 0.017² = 1,488.2, rounded up to 1,489 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.0166                      # observed difference in means
sigma <- 0.161628097158399                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4601480)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,489 (80% power), 1,993 (90% power)
 75% of observed effect: n per arm = 2,646 (80% power), 3,542 (90% power)
 50% of observed effect: n per arm = 5,953 (80% power), 7,969 (90% power)
power.t.test: 1489.1 
Simulated power at n = 1,489 per arm: 0.803 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple intervention-versus-usual-care comparisons and one posted secondary outcome, Prescription Reduction vs Discontinuation Rate. The primary results include an unadjusted p-value for each intervention comparison. No multiplicity adjustment, hierarchy of hypotheses, or strategy for controlling the chance of false-positive findings across comparisons is reported in the registry record. Accordingly, the p-values should be read as unadjusted, rather than as results from a documented family-wise or other multiplicity procedure.

Missing-data methods are not reported. The registry does not state whether outcome data were missing, how missing visits or provider records were handled, or whether any imputation or sensitivity analysis was performed. Nor does it specify the analysis population used for the primary endpoint. The registry enrollment is 309, while the primary outcome results list arm counts of 74, 62, 70, and 77; participant flow and the reason those figures differ are not reported in the registry record.

The endpoint is defined using eligible visits per PCP, but the number of eligible visits per provider is not posted. There is also no reported account of how providers with different numbers of eligible visits contributed to the mean, how repeated visits were handled, or whether clustering within clinics or PCPs was addressed. These are important details for interpreting both the point estimates and their uncertainty in a clinic-assigned study.

The record does not report a statistical analysis plan, covariate adjustment, interim analyses, stopping rules, or methods for handling protocol deviations. The absence of these details does not establish that a particular method was not used; it means the registry record does not document it. These gaps limit independent assessment of the intended and executed analysis.

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

The posted results describe the average proportion of eligible visits per PCP that met the Category 1 definition of appropriate tapering in each randomized arm. The three intervention means were 0.036, 0.027, and 0.019, compared with 0.019 for Care as Usual. The unadjusted comparisons have confidence intervals that include zero and p-values of 0.561, 0.765, and 0.996. Thus, the posted comparisons do not provide a clear distinction from Care as Usual, while the intervals remain compatible with differences in either direction.

These results do not show that the interventions are equivalent to usual care. Demonstrating equivalence or non-inferiority requires an appropriately designed question, margin, and analysis; those are not reported in the registry record. Nor do the results prove that there is no effect. The estimates and intervals describe uncertainty in the posted comparisons, and uncertainty remains substantial.

The outcome is a process measure: it records whether eligible visits involved an MME reduction within the stated threshold and documented consistency with CDC guidelines. It does not establish what happened to an individual patient's pain, function, safety, or longer-term health. The record does not provide those outcomes as part of the primary result. It also does not report the distribution of Category 2 or Category 3 outcomes in the posted primary results.

The study objective concerns PCP prescribing decisions influenced by EHR decision support. The interpretation should stay within that scope. The primary findings alone cannot explain why clinicians made particular decisions, whether the interventions were used as intended, or whether differences in clinic context affected the results. Implementation and analysis details are not reported in the registry record.

For readers, the most defensible takeaway is descriptive: the arm means and unadjusted comparisons are close enough, relative to their uncertainty, that the posted results do not establish a difference from usual care. They also do not establish that all approaches have the same effect or that a clinically important difference can be excluded.

15. Why This Trial Matters Statistically

This trial is statistically interesting because its intervention was assigned at the clinic level while the primary outcome is defined using eligible visits per PCP. That structure raises questions about the unit of analysis, repeated observations, and dependence among outcomes from people working within the same clinic. General statistical context: when observations are correlated, treating them as independent can make uncertainty look smaller than it is. The registry does not describe how these features were handled, making the analysis details important to interpretation.

The endpoint is also a process proportion with a documentation requirement. A visit counted as an appropriate taper only when the MME reduction met the stated threshold and evidence of guideline consistency was documented. That means the measure reflects both the prescribing order and the record of its rationale. The posted result should therefore be understood as a measure of documented prescribing practice, not simply whether a prescription was reduced.

The four-arm structure allows the posted comparisons to distinguish two separate decision-support approaches, their combination, and usual care. But the estimates are accompanied by confidence intervals that cross zero, and the unadjusted comparisons do not resolve whether the arms differ. The result illustrates why effect estimates and precision matter alongside p-values: the direction and plausible magnitude of differences remain uncertain.

Finally, the study's aim is to evaluate a behavioral nudge rather than a forced prescribing rule. Statistical interpretation benefits from keeping the intervention's intended mechanism, the measured process outcome, and patient outcomes distinct. The record supports description of the intervention arms and prescribing measure; it does not report enough analysis or patient-outcome information to extend the primary result beyond that measure.

16. Limitations

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

The registry record gives limited detail about the design and analysis. Although it describes randomization, parallel arms, and clinic assignment, it does not report the number of clinics, the randomization procedure, or whether any stratification or constraints were used. Single masking is listed, but the masked group and masking procedures are not reported. These omissions constrain assessment of how assignment and potential sources of bias were managed.

The primary endpoint is a provider-level proportion based on eligible visits, but eligible-visit denominators and provider-level distributions are not reported. The record does not explain whether provider means were weighted by visit count, how repeated visits were treated, or whether clinic-level correlation was addressed. The reported standard deviations and comparison intervals cannot by themselves resolve these questions.

There is no reported statistical analysis plan, missing-data approach, analysis-population definition, or multiplicity procedure. The record lists 309 enrolled, while endpoint arm counts are 74, 62, 70, and 77; the relationship between those counts is not explained. The registry does not provide enough information to determine whether the figures reflect different populations, exclusions, or another reporting convention.

The primary result is limited to Category 1 appropriate tapering. Although the outcome definition describes inappropriate taper and no taper categories, their arm-level results are not included in the primary outcome figures. The registry lists one secondary outcome, but its results are not reported in the material used for this interpretation. Adverse-event counts are posted as zero in each arm, but definitions, surveillance methods, and additional context are not reported. These limitations counsel against treating the process outcome as a complete account of prescribing or patient experience.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: PRescribing INterventions for Chronic Pain Via the Electronic Health Record Study - Current Opioid-User Population — NCT04601480.
• Registry record last updated 2025-01-30; status last verified 2025-01.
• Results first posted 2025-01-30.
• 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.

20. Record Summary

NCT04601480 is a completed randomized, parallel-group study sponsored by the University of Minnesota. The registry describes a single-masked design and an enrollment of 309. Clinics were assigned to Care as Usual, Choice Architecture Nudge, PMP Integration & Nudge, or the combined approach. The study began on 2020-08-26, with primary completion on 2021-10-01.

The primary endpoint was the mean proportion of opioid-refill-eligible visits per PCP classified as an appropriate taper over 12 months. The posted arm means were 0.019 for Care as Usual, 0.036 for Choice Architecture Nudge, 0.027 for PMP Integration & Nudge, and 0.019 for the combined intervention. All three unadjusted comparison confidence intervals include zero. Further statistical analysis, participant-flow, and missing-data details are not reported in the registry record.