Improving Communication About Pain and Opioids: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Improving Communication About Pain and Opioids (NCT03629197), a randomized na study. The primary outcome is Clinician Number of Targeted Behaviors Per Visit.

2. Clinical Question

3. Trial Design

This was a completed, randomized, parallel-group pilot trial with no masking reported. Clinicians were randomized to communication-skills training or control. The registry describes the intervention as training with standardized patients and the control as receipt of a written summary of opioid prescribing guidelines. The registry lists enrollment of 95; that overall enrollment figure should not be confused with the group counts for each particular outcome.

The design linked clinician assignment to subsequent patient visits. The summary describes recording visits with study clinicians and collecting patient perceptions and health outcomes after the visits. It describes 48 patients as the planned or described patient group for those recordings, while outcome-specific posted counts differ by measure. The primary measure was assessed over a 3-9 month period, depending on how soon appointments with patient participants could be scheduled. Patient pain severity and patient experience were measured at 8 weeks; other secondary measures have their own registry timeframes.

The trial began on 2018-08-15, reached primary completion on 2019-11-05, and is listed as completed. The registry identifies the University of California, Davis as sponsor. The registered purpose was to pilot-test feasibility and generate information for planning a subsequent multisite trial. The registry record does not report the original sample-size justification, the intended statistical analysis plan, or whether any interim analyses were planned.

Because clinicians were randomized but patient outcomes were collected from visits with those clinicians, the assignment structure and the level of measurement differ. The registry record does not describe an adjustment for clustering of patients within clinicians or provide enough detail to establish how that structure was handled in every analysis. The presented summaries should therefore be read as the registry's posted outcome information, not as a complete account of the trial's modeling 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.

Clinician Participants

Reasons for not completing this period:

Patient Participants

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: primary care physicians

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: This baseline module includes data from both patient participants (Communication Skills Training=25, Control=21, Total=46) and clinician participants (Communication Skills Training=21, Control=16, Total=37). The Overall Number of Baseline Participants reflects all participants contributing baseline data (Communication Skills Training=46, Control=37, Total=83).

6. Primary Endpoint

The registry lists the primary outcome as Clinician Number of Targeted Behaviors Per Visit, measured over Over a 3-9 month period (depending on how soon after the intervention clinicians' appointments with patient participants can be scheduled)..

The primary endpoint is the mean number of targeted communication behaviors per recorded visit for primary care physicians. The study team developed a list of behaviors targeted by the intervention and a coding manual to count unique behaviors in each visit. Audio recordings and transcripts were analyzed, with multiple team members measuring behaviors to support reliability of the measure.

This endpoint addresses a proximal question: whether clinicians used communication behaviors that the training was designed to teach. It is not itself a measure of patient pain, opioid prescribing risk, or health improvement. Those topics appear in the trial's stated hypotheses and secondary outcomes, but the primary endpoint focuses on observable communication during the clinical encounter.

Counting behaviors makes it possible to compare the frequency of observed skills between randomized clinician groups. A mean summarizes the average count across recorded visits, while the standard deviation describes how much individual visit counts varied around that average. The registry specifies that visits were assessed over a 3-9 month period, depending on scheduling. That variable interval is relevant when interpreting the endpoint: the timing of recorded visits was not described as identical for every clinician.

The registry describes the measure and its coding process, but does not report a primary inferential analysis, details of any adjustment for clinician-level clustering, or a threshold defining a clinically important difference. The endpoint can therefore be interpreted as a measure of observed communication behavior, while claims about clinical importance or downstream patient benefit require evidence beyond this mean count alone.

7. Results Posted in the Registry

• Communication Skills Training: mean 3.50 versus 2.80 on control; difference 0.70 (95% CI -0.82 to 2.22), standardized effect d = 0.27; z-test p = 0.367.

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.

Compare Efficacy of Control vs Intervention by Measuring Changes in the Severity of Patients Pain Using the Brief Pain Inventory - (Short Form) Pain Severity Subscale Which Measures the Severity of the Patient's Pain.

• 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:
  • Communication Skills Training: mean 6.50 versus 6.00 on control; difference 0.50 (95% CI -0.69 to 1.69), standardized effect d = 0.24; z-test p = 0.408.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Communication Skills Training and the control. The interval gives the range of effects that remain compatible with the data.

Difficult Doctor-Patient Relationship Questionnaire

• 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:
  • Communication Skills Training: mean 25.80 versus 22.80 on control; difference 3.00 (95% CI -3.28 to 9.28), standardized effect d = 0.29; z-test p = 0.349.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Communication Skills Training and the control. The interval gives the range of effects that remain compatible with the data.

Patient Experience Score

• 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:
  • Communication Skills Training: mean -0.10 versus 0.10 on control; difference -0.20 (95% CI -0.70 to 0.30), standardized effect d = -0.22; z-test p = 0.435.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Communication Skills Training and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related but distinct domains: pain severity, the doctor-patient relationship, patient experience, physicians' appraisal of the intervention, and physician communication self-efficacy. The posted numeric summaries include patient pain severity, the Difficult Doctor-Patient Relationship Questionnaire, and Patient Experience Score. Results for every registered secondary outcome are not fully represented by inferential analyses in the registry record.

Across the posted continuous summaries, the group estimates do not form a consistent pattern of clear separation. The uncertainty intervals for the displayed recalculated comparisons include no difference. The Patient Experience Score also has a registry-reported final-value comparison with a confidence interval that includes no difference. Taken together, these results do not provide a precise or consistent secondary-outcome signal that would settle the primary communication question or establish downstream patient benefit.

These measures relate to the primary result because the intervention was intended to change communication, with possible consequences for patients' perceptions and outcomes. But they measure different constructs and timeframes. A change in observed clinician behaviors would not automatically imply a change in pain or patient experience; likewise, a patient measure cannot directly confirm that targeted communication behaviors were used. The secondary outcomes therefore add context rather than serving as interchangeable evidence for the primary endpoint.

Unadjusted secondary comparisons carry less weight when many outcomes may be examined. In general, the more comparisons considered, the greater the chance that some apparent differences arise by chance. The registry record does not report a multiplicity strategy, a hierarchy for secondary hypotheses, or a complete analysis plan. This makes isolated secondary findings especially difficult to interpret as confirmatory. The limited reported analyses and the absence of documented multiplicity handling mean that secondary results are best viewed as exploratory signals for future research, not as independent confirmation of efficacy.

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

• Compare Efficacy of Control vs Intervention by Measuring Changes in the Severity of Patients Pain Using the Brief Pain Inventory - (Short Form) Pain Severity Subscale Which Measures the Severity of the Patient's Pain.
• Difficult Doctor-Patient Relationship Questionnaire
• Patient Experience Score
• Physicians' Overall Appraisal of the Standardized Patient Intervention
• Physician Communication Self-efficacy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a count of targeted behaviors per visit, summarized as a mean and standard deviation. A mean difference compares the group averages on the original measurement scale. Positive values in the posted comparison indicate a higher average in the communication-skills training group than in control. The mean difference of 0.7 is an unadjusted recalculation based on the posted group summaries, rather than a separately reported adjusted model result.

What does the confidence interval describe?

A confidence interval expresses the uncertainty around an estimated difference under the assumptions of the method used. It gives a range of values compatible with the data and method; it is not a guarantee that the true effect lies within that particular interval. For the primary comparison, the interval runs from -0.819 to 2.219. Because it spans zero, the posted summaries are compatible with no mean difference as well as with differences favoring either group. The interval does not establish equivalence, because no equivalence margin is reported.

How should the p-value be read?

The unadjusted p-value is 0.367. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of a difference. This p-value is an unadjusted recalculation, not a registry-reported primary analysis. The registry record does not report a primary inferential model or a prespecified testing plan, so this value should not be presented as the trial's official analysis.

Why does variation matter?

The standard deviations, 2.8 for training and 2.4 for control, describe variation among the observed visit-level counts within each group. When observations vary considerably, the group means are less precisely estimated unless the available information is sufficiently extensive. A mean difference can be small or uncertain even when the group means are not identical. The standard deviation is not a confidence interval and does not show the precision of the estimated difference by itself.

In general, a comparison method also depends on how observations are related. Here, clinicians were randomized, while behaviors were counted during visits with clinicians. If multiple visits or patients are associated with the same clinician, those observations may not be independent. Accounting for such dependence can affect uncertainty estimates. The registry does not report whether or how clustering was handled in the primary analysis, so no particular adjustment should be assumed. This is a limitation in interpreting a recalculation from group-level summaries.

What does an unadjusted recalculation mean?

The recalculated comparison uses the posted means, standard deviations, and outcome-specific group counts to express a simple group difference and its uncertainty. It does not account for any covariates, stratification, clustering, or other features unless those are incorporated in the underlying calculation; the registry record does not report such an adjusted analysis for the primary outcome. Since the discrepancy indicator is false, no conflict with a sponsor-reported primary analysis is identified. Nevertheless, a recalculation from summary statistics is not a substitute for a prespecified trial analysis or an analysis using participant-level data.

For the secondary Patient Experience Score, the registry includes a reported analysis of a final-value mean difference of -0.2, with a 95% confidence interval from -0.7 to 0.2. The separately recalculated interval is -0.702 to 0.302. The registry's own reported result takes precedence over a simple recalculation when the two differ. The registry does not report a p-value or method for that analysis. This distinction illustrates why a recalculated statistic and the trial's reported analysis should not be treated as interchangeable.

The posted results use means and standard deviations for continuous measures. These summaries can be informative, but they do not reveal the shape of each outcome's distribution, the presence of unusual observations, or the full data structure. The registry record does not report diagnostic checks or analysis details sufficient to evaluate those issues. Interpretation should therefore focus on the posted summaries, the stated uncertainty, and the limits of information documented in the registry.

11. Confidence Intervals and Precision

The primary mean difference is 0.7 targeted behaviors per visit, and its 95% confidence interval ranges from -0.819 to 2.219. The interval is wide enough to include a negative difference, no difference, and a positive difference. This means the estimate is imprecise: the observed group difference alone does not tightly determine the direction or size of the underlying difference. The unadjusted p-value of 0.367 is consistent with the interval's inclusion of zero, but the interval is more informative about the range of effects compatible with the data.

Precision is different from whether an estimate is important. The registry does not report a threshold for a meaningful change in behavior counts, so the interval cannot be classified against a trial-defined clinical or practical margin. It also cannot establish that effects within the interval are equally plausible in every substantive sense; it expresses uncertainty under the calculation's assumptions.

The group standard deviations, 2.8 and 2.4, indicate notable spread in observed visit counts relative to the group means. General statistical reasoning says that variability reduces precision when the information available is limited. The outcome-specific group counts are 24 and 21, and the registry does not report missing-data handling or the number of clinician-level clusters used in the analysis. Those omissions limit assessment of the effective information and of the interval's assumptions.

For a pilot study intended to inform future research, imprecision is not unexpected, but it matters: the observed difference should not be treated as a stable estimate for later planning without considering the uncertainty and the possibility that the observed effect overstates or understates the effect in a new study. The interval describes uncertainty around the estimate; it does not answer whether the intervention is beneficial or whether the observed difference would persist in a larger or different setting.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the continuous-outcome comparisons, not total events. They are illustrations based on the observed effect, not the original trial's documented design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of participants per arm that would yield an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the method's assumptions held. The 90% power column expresses the corresponding planning target for a 90% chance. These are planning probabilities, not probabilities that the observed result is correct. The registry's original sample-size rationale and assumptions are not reported in the registry record.

Rows for 100% of the observed effect use the full observed effect as the planning target; rows for 75% and 50% use smaller target effects. The figures rise as the target effect becomes smaller, because smaller group differences are harder to distinguish from random variation. This is a general property of study planning, not evidence that any particular future trial will achieve its target.

These calculations are not observed power. They are prospective planning illustrations derived from the observed effect, and pilot estimates can be unstable. A future study would need to choose a defensible target effect and account for its own design and analysis assumptions. The figures do not show how many participants were enrolled in this trial or prove that the trial was adequately or inadequately sized for its original purpose.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.700; pooled standard deviation σ = 2.622.
2. n = 2 × (1.96 + 0.842)² × 2.622² / 0.700² = 220.2, rounded up to 221 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 <- 0.7                      # observed difference in means
sigma <- 2.62155643455083                     # 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(3629197)
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 = 221 (80% power), 295 (90% power)
 75% of observed effect: n per arm = 392 (80% power), 524 (90% power)
 50% of observed effect: n per arm = 881 (80% power), 1,179 (90% power)
power.t.test: 221.1 
Simulated power at n = 221 per arm: 0.805 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures, including a primary communication-behavior endpoint and secondary outcomes spanning pain, patient experience, relationship quality, physician appraisal, and self-efficacy. When researchers test several outcomes or comparisons, the chance of at least one apparently unusual result can increase. A multiplicity strategy may specify a primary testing hierarchy, adjustment method, or exploratory status for secondary analyses. Such a strategy is not reported in the registry record.

The registry record does not report a detailed statistical analysis plan, the handling of missing observations, or a definition of the analysis population for the primary outcome. It does not state whether all randomized clinicians were included in an intention-to-treat analysis, whether participants were analyzed according to another rule, or how incomplete recordings and patient follow-up were addressed. These details matter because exclusions or missingness can affect both group means and uncertainty. No particular method should be inferred.

The clinician-level randomization and patient-level measurements also make the treatment of dependence important. The record does not report whether the primary or secondary analyses accounted for patients or visits associated with the same clinician. It does not provide enough information to establish whether adjusted models, covariates, or other design features were used. Without those details, the simple unadjusted recalculations should be understood as descriptive analyses of posted summary statistics, not reconstructions of a complete prespecified model.

There is a reported final-value analysis for Patient Experience Score, but the method and p-value are not reported. No other reported analyses are listed for the displayed secondary comparisons. The registry's reporting does not permit a full assessment of which outcomes were formally tested, how testing was prioritized, or whether all planned analyses were reported. These are reporting limitations, not evidence that a particular analysis was or was not performed.

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 lists serious adverse events for the communication-skills training and control groups, with zero serious events reported in each. It also reports zero other adverse events and zero deaths in each group. The numbers at risk for the serious-event summaries are 25 for training and 21 for control; the other-event summaries use the same group-specific counts. No serious-event terms are listed.

These figures describe what was posted for the trial and should be read as counts, not as proof that no harm is possible. A zero count in a study of this scale does not rule out uncommon events, and the registry record does not provide event definitions, attribution judgments, monitoring details, or a statistical comparison of safety between groups. The counts also do not establish that the groups had equivalent safety profiles.

The intervention was clinician training, while the patient-facing outcomes arose through visits with trained or control clinicians. The adverse-event listing does not clarify which participant types were included in each safety denominator or provide further detail about follow-up for safety. The appropriate conclusion is limited: the registry reports no serious adverse events, other adverse events, or deaths in the displayed groups, while the extent to which these data can characterize safety is constrained by the information reported.

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

The posted primary summaries show a higher mean count of targeted communication behaviors per visit in the communication-skills training group than in control: 3.5 versus 2.8. The unadjusted mean difference is 0.7, but its 95% confidence interval, from -0.819 to 2.219, includes no difference. The result therefore describes an observed group contrast with substantial uncertainty; it does not establish that training changed communication behavior.

It also does not show that training reduced high-risk opioid prescribing, increased agreement with treatment plans, or reduced later pain interference. Those were hypotheses described in the registry summary, not the primary endpoint reported in the displayed primary results. The patient secondary measures are related, but they do not provide a substitute for results on each of those specific hypotheses. A behavioral measure is not itself a clinical outcome.

Conversely, the uncertain estimate is not evidence that training had no effect. The interval is compatible with values on either side of zero, and no equivalence margin is reported. The registry also does not document the original power rationale, a complete analysis plan, missing-data methods, or the handling of possible clinician-level clustering. These gaps limit how strongly the summaries can be interpreted.

The trial's stated purpose was to pilot-test feasibility and generate information for planning a subsequent multisite trial. In that setting, the results can help describe the observed behavior counts and the uncertainty around their difference. They should not be treated as definitive evidence of effectiveness, as proof of no effect, or as a direct basis for clinical decisions. The registry record does not establish whether the observed difference is practically important or whether it would persist in a larger study.

17. Why This Trial Matters Statistically

This trial raises a useful statistical issue: the intervention was assigned to clinicians, while the primary outcome was measured in recorded visits. The distinction between the unit of randomization and the level of observed measurement affects how uncertainty should be estimated. If measurements are related through the clinician, treating all observations as independent could misstate precision. The registry record does not say whether this dependence was incorporated in the primary analysis, making the question of analysis structure important to interpreting the result.

The endpoint also illustrates the difference between a mechanistic or process measure and a patient outcome. A count of targeted communication behaviors can indicate whether clinicians used skills emphasized by training. It does not alone determine whether patients experienced better communication, pain, or care. The trial's several outcome domains reflect that causal chain, but each requires its own clearly specified analysis and interpretation.

Finally, the primary estimated difference is accompanied by considerable uncertainty, which is especially relevant for a pilot trial. Planning calculations based on an observed effect can be sensitive to a noisy estimate. Future planning should not treat the point estimate as a guaranteed effect, and should consider the precision, study structure, and outcome-specific missingness. The registry record's purpose of generating data for a later multisite trial makes these statistical issues central to understanding what the pilot can contribute.

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 registry record leaves several trial-specific details unclear. The description of the training's second standardized-patient visit is truncated, so the full intervention content cannot be assessed. The timing of primary-outcome visits varied according to scheduling over a 3-9 month period. The record does not state whether time since training was considered in analysis or whether timing differences could affect the observed behavior counts.

The registry describes clinicians as randomized and patients as recruited through appointments with those clinicians, but does not report how clinician-level assignment and patient-level outcomes were handled in the analysis. It does not document an adjustment for clustering, the analysis population, missing-data methods, or the original sample-size rationale. Outcome-specific counts differ, and the record does not explain why data were unavailable for some outcomes or whether the included observations differed systematically from those not included.

The primary results are group means and standard deviations, with a recalculated unadjusted comparison rather than a reported primary inferential analysis. The registry does not provide participant-level data, model diagnostics, or a clinically meaningful threshold for the behavior count. Consequently, the estimates cannot establish practical importance or support a complete appraisal of model assumptions. Secondary outcomes also have limited reported analyses, and a multiplicity strategy is not documented. These limits should be kept in view when treating the findings as preliminary information for future research.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Improving Communication About Pain and Opioids — NCT03629197.
• Registry record last updated 2026-07-27; status last verified 2026-07.
• Results first posted 2026-07-27.
• 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

The registry record describes a completed randomized parallel-group pilot trial sponsored by the University of California, Davis. Clinicians were assigned to communication-skills training involving standardized patients or to a control condition that received a written summary of opioid prescribing guidelines. Enrollment is listed as 95.

The primary outcome was the mean number of targeted communication behaviors per recorded visit. The posted means were 3.5 for training and 2.8 for control, with an unadjusted recalculated mean difference of 0.7 and a 95% confidence interval from -0.819 to 2.219. The registry's stated aim was to pilot-test the intervention and inform planning for a subsequent multisite trial. Analysis-plan, missing-data, and clustering details are not reported in the registry record.