Alcohol Pharmacotherapy for HIV+ Prisoners: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Alcohol Pharmacotherapy for HIV+ Prisoners (NCT01077310), a randomized na study. The primary outcome is Percentage of Those Maintain or Improve to HIV RNA-1 Viral Load Less Then 400 Copies/mL.

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, quadruple-masked, parallel-group trial sponsored by Yale University. Enrollment was 100. The posted primary outcome includes 67 participants in the intramuscular naltrexone arm and 33 in the placebo arm. The listed phase is NA. The registry record gives the study start as 2010-08 and primary completion as 2015-08.

Participants were HIV-infected prisoners meeting DSM-IV criteria for alcohol dependence or problem drinking. They were transitioning to the community and seeking treatment to prevent relapse to alcohol use. The active intervention was monthly gluteal injections of depot naltrexone, 380mg, over 6 months. The first injection was to be administered before release from prison or jail. The comparator arm was to receive monthly gluteal placebo injections over the same period, with the first injection also before release.

Randomization supports a between-arm comparison in principle, while masking is intended to limit the influence of treatment knowledge on care, reporting, and assessment. The registry does not identify which people or roles were masked, describe the allocation-generation or concealment procedures, or report how treatment adherence was assessed. Those details are not reported in the registry record.

The trial’s stated hypothesis covered HIV outcomes, alcohol treatment outcomes, HIV-related risk behaviors, and reincarceration. The posted primary result is the percentage maintaining or improving HIV viral suppression from baseline to month 6 after release. Secondary outcomes listed include time to alcohol relapse, change in average drinks per drinking day, and change in percent of heavy drinking days. Numerical outcome results for time to alcohol relapse 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Logistic regression backward stepwise models were used to find predictors of HIV viral suppression.

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 Percentage of Those Maintain or Improve to HIV RNA-1 Viral Load Less Then 400 Copies/mL, measured over Baseline to month 6 post release.

The primary endpoint is the percentage of participants who maintained or improved an undetectable HIV viral load from baseline to month 6 after release. The registry defines baseline as the viral load closest to the time of release from incarceration and identifies the threshold as HIV RNA-1 viral load less than 400 copies/mL. Missing lab values were considered to have a detectable viral load.

This endpoint expresses a participant-level binary outcome: each participant is counted according to whether the stated viral-suppression condition was maintained or improved over the follow-up period. A percentage makes the outcome interpretable as the share of the arm meeting that definition. It is not a measure of the size of each participant’s viral-load change, nor does it directly measure alcohol consumption or time to relapse.

Viral suppression is used in this trial as an HIV-related outcome because the study hypothesis included improved HIV outcomes. The endpoint’s meaning depends on the registry’s definition and its handling of missing lab results. Counting missing values as detectable makes the endpoint classification conservative with respect to declaring suppression, but the record does not report how many lab values were missing or whether missingness differed between arms. The posted result therefore describes the outcome under that rule, with uncertainty about the amount and pattern of missing data.

7. Results Posted in the Registry

• Intramuscular Naltrexone: 53.7% (36/67) versus 42.4% (14/33) on control; risk difference 11.3 percentage points (95% CI -9.4 to 32.0), risk ratio 1.27 (0.80–2.00); unadjusted two-proportion z-test p = 0.288.

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.

Alcohol Treatment Outcome: Change in Average Drinks Per Drinking Day

• 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:
  • Extended-release Naltrexone, Received 0-3 Injections: mean -16.60 versus -29.60 on control; difference 13.00 (95% CI -1.15 to 27.15), standardized effect d = 0.54; z-test p = 0.072.
  • Extended-release Naltrexone, Received 4-6 Injections: mean -17.40 versus -29.60 on control; difference 12.20 (95% CI -3.35 to 27.75), standardized effect d = 0.47; z-test p = 0.124.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Extended-release Naltrexone, Received 0-3 Injections and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Extended-release Naltrexone, Received 4-6 Injections and the control. The interval gives the range of effects that remain compatible with the data.

Alcohol Treatment Outcome: Change in Percent of Heavy Drinking Days

• 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:
  • Extended-release Naltrexone, Received 0-3 Injections: mean -38.30 versus -51.30 on control; difference 13.00 (95% CI -10.11 to 36.11), standardized effect d = 0.30; z-test p = 0.270.
  • Extended-release Naltrexone, Received 4-6 Injections: mean -63.60 versus -51.30 on control; difference -12.30 (95% CI -35.87 to 11.27), standardized effect d = -0.31; z-test p = 0.306.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Extended-release Naltrexone, Received 0-3 Injections and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Extended-release Naltrexone, Received 4-6 Injections and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary alcohol outcomes: time to alcohol relapse, change in average drinks per drinking day, and change in percent of heavy drinking days. Numerical arm summaries and unadjusted comparisons are posted for the two change outcomes, but a numerical time-to-relapse result is not reported in the registry record. Across the posted continuous outcomes, the estimates vary in direction across the injection-count strata, and their confidence intervals are broad. That overall pattern does not provide a consistent, precise secondary signal that resolves the uncertainty in the primary HIV endpoint.

These outcomes address different questions from the primary endpoint. Alcohol consumption measures concern changes in drinking, whereas the primary endpoint concerns HIV viral suppression. A result on one outcome does not automatically confirm or contradict a result on another. The trial’s stated hypotheses linked treatment to both HIV and alcohol outcomes, but the record does not report formal analyses that integrate these outcomes or establish a causal pathway between them.

The displayed secondary comparisons are unadjusted, and the registry reports no secondary analyses. Multiple outcomes create multiple opportunities for apparently notable results to arise through chance variation. Without a reported multiplicity strategy, readers cannot determine whether the comparisons were prespecified as confirmatory, whether any adjustment was planned, or how to interpret the collection of p-values as a family. For that reason, secondary numerical patterns carry less evidential weight than a clearly prespecified analysis with a reported multiplicity plan.

The alcohol change summaries also compare groups subdivided by the number of injections received. Because that number is determined after randomization, those strata do not preserve the full protection of the original randomized allocation. The summaries may be informative descriptively, but they should not be treated as direct randomized estimates of the effect of assignment. The registry does not report analyses that account for this post-randomization grouping.

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

• Alcohol Treatment Outcome: Time to Alcohol Relapse
• Alcohol Treatment Outcome: Change in Average Drinks Per Drinking Day
• Alcohol Treatment Outcome: Change in Percent of Heavy Drinking Days

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary at the participant level: a participant either meets the registry’s definition of maintaining or improving undetectable HIV viral load by month 6 after release, or does not. For a binary outcome, an arm percentage describes the proportion classified as meeting the endpoint. A between-arm risk difference describes the contrast between those proportions on the probability scale. The posted primary comparison is a risk-difference comparison, accompanied by a confidence interval and an unadjusted p-value.

What does the confidence interval describe?

In general, a confidence interval gives a range of values compatible with the observed data under the method’s assumptions. It helps show how much uncertainty surrounds an estimate; it is not a range containing a fixed percentage of individual participant outcomes. For the primary risk difference, the interval extends across zero, so the posted data do not pin down whether the underlying difference is positive or negative. The registry does not report an adjusted confidence interval from a fitted treatment-effect model.

What does the p-value add?

In general, a p-value describes how unusual the observed data, or data more extreme, would be under a specified null model. It is not a measure of effect size, clinical importance, or the probability that the null hypothesis is true. The primary unadjusted p-value is 0.288. It should be read alongside the percentages and the interval, rather than as a stand-alone conclusion. The record does not report a sponsor-adjusted primary treatment comparison.

How does the registry describe regression?

The primary endpoint description says that backward stepwise logistic regression models were used to find predictors of HIV viral suppression. Logistic regression is a general method for modeling a binary outcome in relation to explanatory variables. A backward stepwise procedure generally begins with a set of candidate predictors and removes terms according to a selection rule. The candidate variables, selection criterion, final model, coefficient estimates, and model diagnostics are not reported in the registry record. In particular, the description of predictor modeling should not be mistaken for a reported adjusted estimate of the randomized treatment contrast.

Random allocation is relevant because it aims to make treatment groups comparable on average at the outset, but a valid analysis also depends on how participants were retained and analyzed. The analysis population, exclusions after randomization, and handling of treatment discontinuation are not reported in the registry record. Nor does the record state whether a formal intention-to-treat analysis was used. These omissions limit assessment of how closely the posted outcome groups reflect the randomized comparison.

How should the secondary summaries be read?

The two posted continuous alcohol outcomes are changes in average drinks per drinking day and percent of heavy drinking days. Their arm summaries are means with standard deviations. In general, a mean summarizes the average change, while a standard deviation describes variation among participants; it is not the uncertainty interval for the mean. The registry also posts unadjusted mean-difference comparisons and confidence intervals for the injection-count strata.

Those summaries separate participants according to whether they received 0-3 or 4-6 injections. Receipt of a number of injections occurs after randomization, so comparing these strata is not the same as comparing the original randomized arms. Participants’ inclusion in an injection-count stratum may reflect factors related to follow-up, treatment continuation, or other characteristics. The registry does not report an analysis addressing those possibilities. The listed time-to-alcohol-relapse endpoint has no numerical result in the record, and no reported time-to-event analysis is posted.

Why does over-dispersion matter in general?

For count outcomes, over-dispersion means that variability exceeds what a simple model assumes. It can affect standard errors and confidence intervals if the model does not account for it. The primary endpoint is binary, and the posted secondary numerical outcomes are means with standard deviations; no count-model analysis is reported. This is a general statistical consideration, not a claim that over-dispersion was present in this trial.

Finally, the sample-size figures are planning illustrations computed from observed effects, using the stated two-sided significance level of 0.05, equal allocation, and a normal approximation. They are not the trial’s original design justification. The original sample-size assumptions, any planned interim analyses, and the prespecified statistical analysis plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary percentages, 54.0 for intramuscular naltrexone and 42.0 for placebo, are estimates from groups of 67 and 33 participants, respectively. Their difference is uncertain. The confidence interval for the risk difference includes values on both sides of zero, so the posted data do not establish the direction of the underlying difference with precision. The unadjusted p-value is 0.288, which likewise does not provide a precise estimate of the effect’s size.

A confidence interval should be read as an uncertainty range for the estimated contrast, given the method’s assumptions. It is not a guarantee that the true effect lies within the interval, and it does not show the range of responses for individual participants. For this primary result, the interval’s breadth indicates that appreciably different underlying contrasts remain compatible with the data. The registry record does not report an adjusted treatment-effect interval or the details needed to assess a fitted model’s uncertainty.

Precision is influenced by the amount of information in the comparison. The total enrollment was 100, and the primary outcome groups are unequal in size. Missing lab values were counted as detectable, but the count and distribution of missing measurements are not reported. Without that information, readers cannot assess how much the missing-data rule affected the endpoint proportions or whether missingness was balanced between arms.

The secondary mean-difference intervals also span values on both sides of zero. Those ranges indicate substantial uncertainty in the posted comparisons, and the injection-count strata are not randomized contrasts. The registry reports no formal secondary analyses. Taken together, the available intervals are more informative about uncertainty than a binary claim based only on whether a p-value crosses a conventional threshold.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these binary and continuous outcomes, the figures are participants per arm, rather than total events. The calculation assumptions stated in the record are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes a planning target: under the stated assumptions and a specified effect size, it is the approximate number of participants per arm needed for an 80% chance of detecting that effect using the assumed test. The 90% power column uses a higher chance of detection as its target and therefore generally calls for more participants per arm. These are conditional planning quantities, not guarantees that a future study will achieve that power; actual results depend on the true effect, variability, adherence, missingness, and analysis.

For the primary binary outcome, planning for 100% of the observed effect gives 306 participants per arm for 80% power and 409 participants per arm for 90% power. Planning for 75% of the observed effect gives 543 and 726 participants per arm, respectively. Planning for 50% of the observed effect gives 1,216 and 1,627 participants per arm, respectively. The pattern illustrates why smaller target effects require more participants: a smaller contrast is harder to distinguish from sampling variation.

These illustrations are not observed power. Observed power is not a useful substitute for reading the estimated effect and its confidence interval after a trial. The planning figures instead show how sample requirements change under the stated assumptions and effect-size scenarios. They should not be read as a retrospective judgment that the trial was designed to meet these particular targets.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.424; treatment proportion p₁ = 0.537; average p̄ = 0.481.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7066 = 1.3849.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7020 = 0.5909.
4. n = (1.3849 + 0.5909)² / (0.1131)² = 305.3, rounded up to 306 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.424242424242424                          # control proportion
p1 <- 0.537313432835821                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1077310)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 306 (80% power), 409 (90% power)
 75% of observed effect: n per arm = 543 (80% power), 726 (90% power)
 50% of observed effect: n per arm = 1,216 (80% power), 1,627 (90% power)
power.prop.test: 305.3 
Simulated power at n = 306 per arm: 0.798 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The record lists a primary HIV viral-suppression endpoint and several secondary outcomes covering alcohol relapse and drinking patterns. It does not report whether a multiplicity procedure was planned or applied. Multiplicity matters because testing several outcomes or contrasts increases the opportunity for chance findings. Without a stated hierarchy, adjustment method, or distinction between confirmatory and exploratory analyses, isolated secondary p-values should be interpreted cautiously.

The primary endpoint description does specify one missing-data rule: missing lab values were considered to have a detectable HIV viral load. That rule directly affects classification of the binary endpoint. The number of participants with missing lab values, reasons for missingness, timing of missing measurements, and distribution across arms are not reported in the registry record. Methods for missing values in the secondary alcohol outcomes are also not reported.

The registry states that backward stepwise logistic regression models were used to find predictors of viral suppression. It does not report the predictor variables, selection criterion, final model, adjusted estimates, or diagnostics. The record also does not report the analysis population, the handling of participants who received fewer injections than planned, or whether analyses followed randomized assignment. These details matter when interpreting estimates because exclusions, missing observations, and post-randomization treatment exposure can affect comparability.

Information about interim analyses, stopping rules, and the original statistical analysis plan is not reported in the registry record. It is therefore not possible to establish from the registry entry how outcome selection, multiplicity, missingness, and model choice were prespecified or handled beyond the stated missing-lab rule. These are reporting limitations; they do not, by themselves, demonstrate that an inappropriate method was used.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero participants affected by serious adverse events in each arm: 0 of 67 for extended-release naltrexone and 0 of 33 for placebo. It lists 9 participants with other, non-serious adverse events in the naltrexone group and 2 in the placebo group. These are counts of participants affected, not counts of every event occurrence.

No serious adverse-event terms are listed. The death fields are not reported in the registry record, so the entry does not establish a death count. The posted adverse-event counts describe what the registry records during the specified study reporting; they do not show whether an event was caused by treatment, how severe non-serious events were, or whether reporting was complete. The record does not provide event-level descriptions or comparative statistical analyses. In particular, the zero serious-event counts should be read as recorded counts in these groups, not as proof that serious events cannot occur.

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

The primary result shows that 54.0 of participants in the intramuscular naltrexone arm and 42.0 in the placebo arm met the registry’s definition of maintaining or improving undetectable HIV viral load through month 6 after release. The observed direction favors a higher percentage in the naltrexone arm, but the estimate is imprecise: the confidence interval for the risk difference includes values in both directions, and the unadjusted p-value is 0.288.

These findings do not establish that naltrexone improves HIV viral suppression, and they do not establish that the treatments have identical effects. An uncertain estimate can be compatible with more than one underlying effect. The result is also tied to a specific endpoint definition, follow-up period, participant group, and missing-lab rule. It does not directly measure viral-load changes in all participants or establish an effect on alcohol relapse, drinking behavior, risk behaviors, or reincarceration.

The study hypothesis included several HIV and alcohol outcomes, but the registry does not report a full set of comparative analyses. In particular, the time-to-relapse result and adjusted predictor-model results are not reported. Secondary outcome summaries are divided by injection count, a post-randomization measure, and therefore are not equivalent to a comparison based solely on randomized assignment.

General interpretation of a randomized trial also depends on whether participants are analyzed according to assignment, how missing data are handled, and whether the planned analysis is reported. The registry provides the missing-lab classification rule but not the amount of missingness or the full analysis population. These gaps limit how far the posted summaries can support conclusions. The appropriate statistical reading is descriptive: the observed primary percentage was higher in the naltrexone arm, with considerable uncertainty and no reported adjusted treatment analysis.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to interpret a randomized comparison when the posted endpoint is a proportion and the groups are unequal in size. Arm percentages are easy to read, but the contrast and its uncertainty are essential: the observed percentages differ, while the confidence interval spans both possible directions. Reporting the interval alongside the arm summaries prevents the observed contrast from being mistaken for a precise estimate.

The endpoint also makes missing-data handling visible. Treating missing viral-load measurements as detectable defines how those participants enter the binary result, but the number and pattern of missing observations are not reported. A transparent rule is valuable, while the absence of missingness counts leaves readers unable to judge its practical influence.

The registry’s mention of backward stepwise logistic regression illustrates why describing a method is not the same as reporting an analysis. Without the model specification and results, readers cannot evaluate adjustment, predictor selection, or the relation between the model and the randomized treatment comparison. Likewise, listing several outcomes without a stated multiplicity approach makes it harder to distinguish confirmatory evidence from exploratory patterns.

Finally, the secondary summaries are stratified by injections received. This highlights a common distinction between randomized assignment and treatment exposure after randomization: the latter can be associated with participant characteristics and follow-up, so those comparisons may not retain the same causal interpretation. The record’s limitations make this trial a useful example of why effect estimates, uncertainty, missing-data rules, analysis populations, and reporting completeness all matter together.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The posted primary result is based on 67 participants in the naltrexone arm and 33 in the placebo arm, with a wide uncertainty range for the risk difference. The registry does not report an adjusted treatment-effect analysis, despite describing backward stepwise logistic regression for finding predictors of viral suppression. The final model and its estimates are not available in the record.

Missing lab values were classified as detectable, but the number of missing values and their distribution across arms are not reported. This prevents assessment of how much the rule influenced the percentages. The record also does not state the analysis population, the treatment of withdrawals or protocol deviations, or whether participants were analyzed according to randomized assignment.

The secondary alcohol summaries are organized by injections received rather than only by randomized arm. Because injection receipt occurs after randomization, such strata can differ for reasons other than assigned treatment. No reported analysis addresses this concern. The time-to-alcohol-relapse endpoint is listed, but its numerical result and analysis are not reported in the registry record.

Several relevant design and analysis details are absent, including the original sample-size justification, the prespecified statistical analysis plan, multiplicity handling, interim analyses, allocation procedures, and the identities of masked roles. The trial followed participants through month 6 after release for the primary endpoint; the registry does not report longer-term primary results. These limitations concern the scope and transparency of the available record and should not be taken as evidence that unreported procedures were necessarily inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Alcohol Pharmacotherapy for HIV+ Prisoners — NCT01077310.
• Registry record last updated 2017-05-30; status last verified 2017-04.
• Results first posted 2016-11-25.
• 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 describes a completed randomized, quadruple-masked, parallel-group study of extended-release intramuscular naltrexone versus intramuscular placebo among HIV-infected prisoners with alcohol dependence or problem drinking who were transitioning to the community. Enrollment was 100. The primary outcome was the percentage maintaining or improving undetectable HIV viral load from baseline to month 6 after release, with missing lab values considered detectable.

The posted primary percentages were 54.0 for naltrexone and 42.0 for placebo. The unadjusted p-value was 0.288, and the risk-difference confidence interval extended across zero, indicating substantial uncertainty about the direction and size of the underlying contrast. The registry also posts secondary drinking-change summaries, but not a numerical time-to-relapse result or reported secondary analyses. The record does not provide an adjusted treatment estimate, a complete missing-data account, or the trial’s original statistical plan.