Treating Chronic Pain and Depression in HIV+ Patients in Primary Care Settings: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treating Chronic Pain and Depression in HIV+ Patients in Primary Care Settings (NCT01735708), a randomized na study. The primary outcome is Brief Pain Inventory Interference Scale at 3 Months.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. It lists the phase as NA and the status as completed. Butler Hospital is named as sponsor. Enrollment is listed as 187. The study start is recorded as 2012-11, and primary completion as 2014-08.

Participants were assigned to HIVPASS or health education. Both arms involved seven individual sessions, but their stated content differed: HIVPASS addressed pain interference and depression management and began with a collaborative meeting with the primary care physician, while health education sessions each focused on a different education topic. These descriptions establish the intended contrast, but the registry record does not report the randomization procedure, allocation concealment, or whether other aspects of care were standardized.

The posted primary outcome results report 79 participants in each arm. For the 12-month pain interference measure and depression measure, the posted health education group size is 84 and the HIVPASS group size is 79. The registry record does not explain the relationship between these outcome-specific group sizes, the enrollment figure, or the analysis populations. These figures should therefore be read as the reported counts for the outcomes, not as a complete account of participant flow.

The registry identifies one primary outcome at 3 months and three secondary outcomes: pain interference at 12 months and depression symptoms at 3 and 12 months. The record does not report the intended original sample-size assumptions, a detailed protocol, or the procedures used to handle missing outcome observations.

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 Brief Pain Inventory Interference Scale at 3 Months, measured over 3 months.

The primary endpoint was the Brief Pain Inventory Interference Scale at 3 months. The registry describes it as a self-report measure of interference due to pain, scored on a scale ranging from 0-10. Higher scores represent a worse outcome. This endpoint therefore concerns the impact of pain on a person’s activities and functioning, rather than pain intensity alone.

A continuous score preserves gradations in reported interference. Comparing group means can describe differences in average scores, while the standard deviation indicates how much scores vary within each group. These summaries are useful for describing the observed outcome, but they do not by themselves establish whether an intervention caused a difference. Interpretation also depends on the analysis method, uncertainty, outcome timing, missing observations, and the clinical relevance of a score difference.

The posted primary group means were 5.03 for health education and 4.23 for HIVPASS, with standard deviations of 2.98 and 2.84, respectively. The simple unadjusted mean difference is reported as -0.8. Since higher scores represent worse interference, the group means are directionally lower in the HIVPASS arm. The registry’s own mixed-model result is a different estimate and is the relevant sponsor-reported analysis for interpreting the trial’s primary comparison.

7. Results Posted in the Registry

• HIVPASS Intervention: mean 4.23 versus 5.03 on control; difference -0.80 (95% CI -1.71 to 0.11), standardized effect d = -0.27; z-test p = 0.084.

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.

Brief Pain Inventory Interference Scale at 12 Months

• 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:
  • HIVPASS Intervention: mean 4.95 versus 4.74 on control; difference 0.21 (95% CI -0.73 to 1.15), standardized effect d = 0.07; z-test p = 0.662.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HIVPASS Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Quick Inventory of Depression Symptoms at 3 Months

• 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:
  • HIVPASS Intervention: mean 10.25 versus 10.35 on control; difference -0.10 (95% CI -1.60 to 1.40), standardized effect d = -0.02; z-test p = 0.896.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HIVPASS Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Quick Inventory of Depression Symptoms at 12 Months

• 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:
  • HIVPASS Intervention: mean 9.80 versus 10.18 on control; difference -0.38 (95% CI -2.02 to 1.26), standardized effect d = -0.07; z-test p = 0.650.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HIVPASS Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover pain interference at 12 months and depression symptoms at 3 and 12 months. Across these outcomes, the sponsor-reported estimates do not provide a consistent pattern of statistically clear separation between arms: their 95% confidence intervals include zero. The simple comparisons of the posted group means likewise do not show intervals that exclude zero. This overall pattern does not independently reinforce the primary sponsor-reported finding.

The secondary outcomes address related but distinct questions. Pain interference measured at 12 months concerns persistence of the pain-related outcome, while the depression scores address a different symptom measure at follow-up. The registry’s primary comparison is pain interference at 3 months. Differences in outcome and timing mean that secondary results should not be treated as direct replications of the primary result.

These analyses also carry less evidential weight because they are secondary and because the registry record does not report whether or how multiplicity was addressed. When several outcomes and time points are examined, the chance of finding an apparently notable result can increase if interpretation focuses on isolated comparisons. Unadjusted p-values do not account for that broader set of analyses. The record lists four outcome measures and four analyses, but does not describe a prespecified hierarchy beyond identifying the primary endpoint.

The secondary results therefore help describe the range of outcomes recorded, but they should not be used to claim broad effects across pain and depression. Their interpretation is constrained by uncertainty, the absence of multiplicity details, and unreported missing-data and analysis-population procedures.

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

• Brief Pain Inventory Interference Scale at 12 Months
• Quick Inventory of Depression Symptoms at 3 Months
• Quick Inventory of Depression Symptoms at 12 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a score on a scale, summarized by a mean and standard deviation. A mean describes the group’s average score, while a standard deviation describes the spread of individual scores around that average. These statistics provide a compact account of the observed distributions, but they do not show the full shape of those distributions or whether unusual values were present.

What does a mean difference represent?

A mean difference expresses the separation between two group averages in the original score units. For the simple primary recalculation, the HIVPASS mean is compared with the health education mean, and the estimate is -0.8. The negative sign reflects the ordering used for that recalculation; it is not a probability or a percentage. Because higher Brief Pain Inventory Interference Scale scores represent worse outcomes, lower scores indicate less reported interference. The registry’s model-based mean difference (net) is a separate estimate produced by the sponsor’s analysis.

Why distinguish the simple comparison from the reported model?

A simple comparison calculated from group means and standard deviations is unadjusted. A mixed model can use a different structure for the analysis and may account for repeated measurements or other modeled features, but the registry record does not describe the model specification, covariates, or assumptions. Those details cannot be inferred from the method label alone. The two estimates should not be treated as interchangeable. Since the record flags a discrepancy, the sponsor’s analysis takes precedence for the trial’s reported inference; the unadjusted calculation is best read as a transparent check based on posted summary statistics.

How should the confidence interval and p-value be read?

A confidence interval describes the uncertainty around an estimated effect under the analysis assumptions. It gives a range of values compatible with the data and model at the stated confidence level; it is not a range containing a guaranteed share of individual outcomes. For the sponsor-reported primary analysis, the 95% interval is from -2.28 to -0.34. For the simple recalculation, the interval is from -1.708 to 0.108. The different intervals reflect the different estimates and methods. A p-value describes how unusual the observed data, or more extreme data, would be under a specified null model; it is not the probability that the null hypothesis is true and does not measure clinical importance.

What can the standard deviations tell us?

The posted primary standard deviations, 2.98 and 2.84, describe variation in scores within the two arms. A mean difference can be modest relative to this person-to-person variability even when an analysis estimates a group contrast. Conversely, a small p-value does not make the score distributions non-overlapping or imply that every participant experienced a similar outcome. The registry record does not provide individual-level data or distribution plots from which to assess those features.

Why does over-dispersion matter in other kinds of outcomes?

As a general statistical point, over-dispersion arises when observed variability is greater than a model assumes. It can make standard errors too small if ignored, producing confidence intervals that are too narrow and p-values that are too optimistic. This trial’s listed primary and secondary outcomes are continuous scores, and the registry does not report an over-dispersion assessment. The concept is relevant to statistical modeling generally, but it should not be presented as a feature established for this trial.

What does randomization contribute?

Random assignment is intended to make comparison groups similar on average with respect to factors that could affect the outcome. It does not guarantee balance in every characteristic, and its protection depends on implementation and follow-up. The registry identifies the allocation as randomized but does not report the sequence-generation procedure, concealment details, or baseline characteristics in the registry record recorded for this analysis. The record therefore supports describing the trial as randomized, but not evaluating those specific safeguards.

Finally, the analysis population and handling of missing observations can affect estimates, particularly when outcome availability differs between arms or over time. The registry record does not report those details. The reported group summaries and mixed-model results can be described as posted, but the unreported analysis procedures limit independent assessment of how the estimates were obtained.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the observed data and analysis. A confidence interval is a useful indicator: narrower intervals indicate less statistical uncertainty under the model, while wider intervals leave more plausible values compatible with the data. The 95% confidence interval for the registry’s primary mixed-model estimate is from -2.28 to -0.34. It excludes zero, whereas the interval for the unadjusted recalculation, from -1.708 to 0.108, includes zero. These are not competing versions of the same analysis; they arise from different methods, and the discrepancy means the sponsor’s own analysis takes precedence.

The interval’s position relative to zero addresses statistical compatibility with no group difference, not clinical importance. The record does not report a threshold for a clinically meaningful change in pain interference, so the confidence interval cannot establish whether all or part of its range represents an important benefit to participants. Nor does it describe the range of individual responses.

Precision should also be considered in light of the outcome-specific counts. The primary summaries report 79 participants in each arm; other posted outcomes have different group counts. The registry record does not explain missing observations, their reasons, or how they entered the model. Those omissions limit assessment of whether the reported uncertainty fully reflects the data available at each time point.

The confidence interval is conditional on the model and analysis assumptions. Since the model specification is not reported, readers cannot fully assess those assumptions or reproduce the sponsor analysis. Thus, the primary sponsor result is statistically more precise than a statement based on the point estimate alone, but its interpretation remains bounded by the reporting detail and the difference from the unadjusted recalculation.

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 illustrative calculations based on the observed effect, not the trial’s own original design. For these continuous outcomes, the figures represent participants per arm, not a combined total or a total number of events. The 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 trial’s original sample-size justification and assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm the planning calculation would require for an 80% chance of detecting the specified effect under those assumptions, if that effect and the other assumptions were correct. The 90% power column gives the corresponding planning figure for a 90% chance. These are design targets, not guarantees that a future study will produce a significant result.

Rows using 100%, 75%, and 50% of the observed effect illustrate how the planning requirement changes when the target effect is smaller. Smaller effects need more participants to detect with the same power under the stated assumptions. The figures can become especially large when the observed effect is close to zero; this reflects the difficulty of distinguishing a very small effect from random variation, rather than demonstrating that a large trial would necessarily find a meaningful result.

These are planning illustrations, not observed power. They do not revise the trial’s actual design or explain the discrepancy between the sponsor’s primary analysis and the simple recalculation. Their usefulness depends on the effect estimate being a reasonable basis for future planning, which may be uncertain when the observed estimate is imprecise or differs by analysis method.

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 = -0.800; pooled standard deviation σ = 2.911.
2. n = 2 × (1.96 + 0.842)² × 2.911² / -0.800² = 207.8, rounded up to 208 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 <- -0.8                      # observed difference in means
sigma <- 2.9108418026406                     # 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(1735708)
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 = 208 (80% power), 279 (90% power)
 75% of observed effect: n per arm = 370 (80% power), 495 (90% power)
 50% of observed effect: n per arm = 832 (80% power), 1,113 (90% power)
power.t.test: 208.8 
Simulated power at n = 208 per arm: 0.798 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a mixed-model mean difference (net) of -1.31, with a 95% confidence interval from -2.28 to -0.34 and p = 0.008. The simple unadjusted recalculation from the posted group summaries is -0.8, with a 95% confidence interval from -1.708 to 0.108 and an unadjusted p-value of 0.084. The two approaches therefore produce different estimates and different conclusions about whether the interval includes zero.

The discrepancy flag is true. Under the stated reporting approach for this trial, the sponsor’s own analysis takes precedence; the recalculation is a check based on posted summary statistics, not a replacement for the mixed model. A mixed model may differ from a comparison of endpoint means, but the registry record does not report enough model detail to identify the reason for this particular difference or to reproduce the analysis.

Accordingly, the sponsor result should be cited as the trial’s reported primary inference, while the recalculation should be described as an unadjusted result from the summary data. Neither estimate alone establishes causation or clinical importance. The scale’s direction is known—higher scores mean worse interference—but the registry does not state the mixed-model contrast coding in enough detail to resolve the sign convention independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and three secondary outcomes, and lists four analyses. The primary outcome is pain interference at 3 months; secondary outcomes are pain interference at 12 months and depression symptoms at 3 and 12 months. The record does not report whether a formal testing hierarchy, family-wise error procedure, or other multiplicity adjustment was prespecified or used.

Multiplicity matters because interpreting several statistical tests creates more opportunities for a result to appear notable by chance. A primary outcome specified in advance can help focus interpretation, but it does not by itself resolve how multiple secondary comparisons should be judged. The reported secondary p-values should therefore be read as individual, unadjusted results unless the registry record documents otherwise; it does not.

Information about missing data is also limited. The outcome summaries list different group counts at different time points. The record does not report why observations are absent, whether missingness differed by arm, how missing values were handled, or whether sensitivity analyses were conducted. These matters are important because an analysis relying on observed outcomes can be affected if the availability of measurements relates to participants’ outcomes or treatment assignment.

The registry record does not identify the analysis population in detail, such as whether the model included all randomized participants or only participants with available measurements. It also does not report a participant flow description sufficient to connect enrollment with each outcome-specific count. The listed numbers should be treated as the posted analysis counts for those outcomes, without assuming how the analysis population was defined.

Finally, the mixed-model method is named, but its specification is not reported. Details of covariates, covariance structure, model diagnostics, and any adjustments cannot be inferred. These reporting gaps do not erase the posted results, but they limit independent evaluation of multiplicity, missingness, model assumptions, and reproducibility.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: dyspnea (5.3%), surgical or medical procedure (5.3%), hospitalization/reason unknown (4.2%), seizure (4.2%), lung infection (3.3%).

The registry lists serious adverse events among participants at risk in each arm. For health education, 39 of 95 are reported as affected by serious adverse events; for HIVPASS, 21 of 92 are reported as affected. Other adverse events are listed for 40 of 95 in health education and 35 of 92 in HIVPASS. The record also lists 2 deaths in each arm.

These are descriptive counts and denominators as recorded, not adjusted comparisons. They do not establish that an intervention caused an event or that a difference between arms is meaningful. The registry does not report event attribution, timing, severity details beyond the serious-event classification, or whether participants could contribute more than one event. The listed deaths should not be attributed to either intervention based on this information alone.

The most frequently listed serious-event terms include Dyspnea and Surgical or medical procedure, each reported as 5.3%; Hospitalization/reason unknown and Seizure, each 4.2%; Lung infection, 3.3%; and Chest pain, 2.2%. The record does not provide further context for these terms in the listed summary. These safety data should be read alongside the limited reporting detail, rather than as a complete account of comparative risk.

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

The primary sponsor-reported analysis indicates a difference between the trial arms on pain interference at 3 months under the mixed-model analysis: the estimated mean difference (net) is -1.31, and its 95% confidence interval excludes zero. The score is a self-report measure on which higher values represent worse interference. The result is a group-level statistical finding, not a statement that every participant experienced improvement or that the size of the difference is important to each person.

The simple unadjusted recalculation from posted group means gives a different estimate and an interval that includes zero. Because the discrepancy flag is true, the sponsor’s analysis takes precedence as the reported trial result. The registry record does not explain the source of the disagreement or provide the model specification needed for independent replication. This limits how fully readers can assess why the analyses diverge.

The results do not establish that HIVPASS is superior to every alternative, since the comparator was a health education program with its own individual sessions. They do not show how the intervention compares with no intervention or usual care. Nor do the posted data establish effects beyond the stated outcomes and assessment times. Secondary outcomes do not provide clear independent confirmation, and the registry does not report adjustment for multiple comparisons.

Statistical evidence of a difference is distinct from evidence of clinical importance. The registry record does not give a threshold for a meaningful score change, nor does it report participant-level response patterns. The group means and model estimate cannot show whether the same people experienced changes in pain interference and depression symptoms or how benefits and harms were distributed.

Finally, the record leaves important design and analysis details unreported, including missing-data handling, analysis populations, and model specification. The results can be described as posted, but their interpretation should remain specific to this trial’s randomized comparison and the information documented in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why a reported model estimate and a simple recalculation from group summaries may not agree. The posted primary group means and standard deviations support an unadjusted comparison, while the registry also reports a mixed-model analysis. Here, those approaches yield different estimates and different confidence-interval conclusions. Distinguishing the sponsor’s analysis from the recalculation prevents readers from treating a summary-statistic check as if it reproduced the original model.

The example also shows why the endpoint’s scale direction matters. Higher scores represent worse pain interference, so a lower mean has a different interpretation from a higher one. Even so, the sign of a model-based contrast must be read with its coding convention in mind, which is not fully reported in this record.

Precision and clinical importance are separate questions. The sponsor’s interval excludes zero, but the record does not define a meaningful-change threshold. The interval therefore informs statistical uncertainty without deciding whether the estimated difference matters in participants’ lives. The secondary outcomes, meanwhile, do not form a clear pattern of supporting evidence, and multiplicity procedures are not reported.

For clinical researchers, these details matter because conclusions depend not only on the point estimate, but also on analysis choices, uncertainty, comparator, timing, and reporting completeness. The trial offers a concrete case for keeping descriptive summaries, model-based inference, safety counts, and planning calculations conceptually distinct.

19. 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 trial-specific limitations follow from the registry record’s reporting gaps. The randomization is identified, but the method used to generate the allocation sequence and conceal assignments is not reported. The record also does not report baseline characteristics in the registry record recorded for this analysis, limiting assessment of group comparability beyond the randomized design label.

The primary sponsor analysis differs from the simple unadjusted recalculation. The record does not explain the difference or provide the mixed-model specification, so the model-based result cannot be independently reconstructed from the posted summary statistics. The sponsor result takes precedence, but this reporting gap limits assessment of its assumptions and the source of the discrepancy.

The outcome-specific counts differ across measures and follow-up times, and the record does not explain those counts or describe missing-data procedures. The analysis population, reasons for unavailable measurements, and sensitivity analyses are not reported. These omissions limit assessment of whether incomplete outcome data could have influenced the results.

The registry does not report a multiplicity plan for the primary and secondary analyses. The secondary findings therefore require caution when viewed together. It also does not state a clinically meaningful threshold for the primary scale, making it difficult to judge the practical importance of the estimated difference from the posted results alone.

For safety, the record lists counts, denominators, terms, and deaths, but does not report event attribution or timing. The adverse-event summaries consequently cannot establish comparative causality. Finally, the study concerns a specific intervention and health education comparator delivered in individual sessions in primary care settings; the registry information does not establish how the findings generalize beyond this trial context.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Treating Chronic Pain and Depression in HIV+ Patients in Primary Care Settings — NCT01735708.
• Registry record last updated 2022-10-13; status last verified 2022-09.
• Results first posted 2022-10-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized, unmasked, parallel-group trial sponsored by Butler Hospital, with enrollment listed as 187. It compared seven-session HIVPASS with seven-session health education for HIV-positive patients in primary care settings. The primary outcome was pain interference at 3 months.

The sponsor-reported mixed-model primary estimate was -1.31, with a 95% confidence interval from -2.28 to -0.34 and p = 0.008. A simple unadjusted recalculation differs, and the discrepancy flag is true; the sponsor’s own analysis takes precedence. Three secondary outcomes were also posted, without reported multiplicity procedures. Missing-data methods, analysis populations, and mixed-model details are not reported in the registry record.