Integrated PrEP Interventions for People Who Inject Drugs in Rural Kentucky: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Integrated PrEP Interventions for People Who Inject Drugs in Rural Kentucky (NCT05037513), a randomized na study. The primary outcome is Number of Participants Initiating PrEP.

2. Clinical Question

The clinical question is about whether the intervention groups differed in the recorded initiation outcome during the specified follow-up period. It is not a comparison of later adherence, duration of PrEP use, or HIV outcomes. Those questions are not reported as primary outcomes in the registry record. The endpoint is a count of participants with documented initiation, so the group results describe event counts and the relative frequency of the recorded event, not the quality or duration of PrEP use.

The registry describes an aim to assess feasibility, acceptability, and preliminary efficacy, alongside work on adapting the intervention and understanding barriers and facilitators to its integration into syringe service program practice. The posted primary outcome addresses the initiation component of that broader aim. The comparison therefore needs to be read as an estimate of initiation in these intervention settings, with attention to the size and precision of the observed difference and to the analysis population used.

3. Trial Design

The registry record describes a completed randomized, parallel-group behavioral intervention study with no masking. The enrollment is listed as 80. The record identifies HIV prevention as the condition and gives the study title as “Integrated PrEP Interventions for People Who Inject Drugs in Rural Kentucky.” The sponsor is listed as Hilary L Surratt, PhD.

Participants were assigned to CDC-PrEP or SBCM-PrEP. CDC-PrEP consisted of one session of PrEP education based on CDC guidelines, delivered one on one by an Advanced Practice Registered Nurse in a syringe service program setting. SBCM-PrEP consisted of a multi-session Strengths-Based Case Management intervention adapted to include PrEP-related educational content, delivered one on one by an Advanced Practice Registered Nurse in the same type of setting. The comparison therefore concerns two behavioral service approaches, not a medication-versus-placebo comparison.

The registry lists the study start as 2021-09-16, primary completion as 2024-04-09, and status as completed. These dates describe the record’s study milestones; they do not by themselves explain recruitment progress, follow-up completeness, or the timing of individual assessments. The registry record does not report the trial’s original sample-size justification or the design assumptions used to choose its enrollment target.

The posted primary results are for a per-protocol population, defined in the record as participants with any exposure to their respective interventions. The record says that both intent-to-treat and per-protocol populations were analyzed, while identifying the per-protocol results as those reported. The arm counts in the primary outcome results are 38 for CDC-PrEP and 39 for SBCM-PrEP. These analysis counts should not be confused with the registry’s enrollment entry, because they refer to the posted per-protocol outcome results.

The record also lists intervention engagement and intervention satisfaction as secondary outcomes. It does not report enough detail to infer how allocation was generated, whether allocation was concealed, how fidelity was assessed, or how deviations from the assigned intervention were handled.

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.

Intervention Period

Reasons for not completing this period:

Follow Up Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: We analyzed both the intent to treat (ITT) and per protocol populations. Per protocol is reported here, which includes those with any exposure to the respective interventions.

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 Number of Participants Initiating PrEP, measured over 3 months post-baseline.

The primary endpoint is the number of participants initiating PrEP, assessed at 3 months post-baseline. Initiation is defined as documented dispensing of a PrEP prescription. In the posted per-protocol results, the event count is 1 in the CDC-PrEP group and 6 in the SBCM-PrEP group. The corresponding group sizes are 38 and 39, respectively.

A documented dispensed prescription provides a concrete record-based indicator that a participant initiated PrEP during the endpoint assessment period. It is distinct from outcomes such as expressing interest, receiving education, being referred, or continuing PrEP over time. The definition makes the outcome interpretable as a recorded initiation event, while also limiting what it can establish: the registry’s primary endpoint does not measure subsequent adherence, persistence, or clinical outcomes.

The endpoint is a binary event at the participant level, summarized as counts within each group and compared using measures of group difference and association. Because the event counts are limited, the estimated contrast can be sensitive to a small number of outcomes, and its uncertainty is important to consider alongside the point estimate. The registry record does not report further details about the process for confirming prescription dispensing or resolving missing endpoint documentation.

7. Results Posted in the Registry

• SBCM-PrEP: 15.4% (6/39) versus 2.6% (1/38) on control; risk difference 12.8 percentage points (95% CI 0.3 to 25.2), risk ratio 5.85 (0.74–46.30); unadjusted two-proportion z-test p = 0.052.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either had documented PrEP initiation during the specified assessment period or did not. The registry summarizes this outcome as counts in each group. With a binary outcome, a group proportion represents the fraction of participants in that group who experienced the recorded event. The posted proportions are 0.026 for CDC-PrEP and 0.154 for SBCM-PrEP.

What does the risk difference describe?

The risk difference subtracts the event proportion in the comparator group from the event proportion in the intervention group. It is an absolute measure: it expresses how far apart the groups are on the event-proportion scale. The recalculated risk difference is 0.128, with a 95% confidence interval from 0.003 to 0.252. The estimate is based on the posted group summaries and is unadjusted. It describes the observed contrast in this per-protocol comparison, not a guaranteed difference in another population or setting.

What do the odds ratio and risk ratio describe?

The odds ratio compares the odds of documented initiation between the groups. The registry reports a logistic regression odds ratio of 7.06, with a 95% confidence interval from 0.8 to 62.2. The unadjusted recalculation gives an odds ratio of 6.727, with a confidence interval from 0.769 to 58.82. The posted recalculated risk ratio is 5.846, with a confidence interval from 0.738 to 46.3. Odds ratios and risk ratios are relative measures; they do not express the absolute difference in event proportions. When an outcome is uncommon, the odds ratio and risk ratio may be numerically similar, but they remain different measures and should not be treated as identical.

Why can analyses of the same outcome differ?

A logistic regression analysis can estimate an odds ratio using a model, while the recalculated unadjusted estimate uses only the posted group counts and sizes. Adjustments, model choices, and other analysis details can affect estimates and uncertainty. The registry record does not report the full model specification or covariates for the logistic regression result. It reports an odds ratio of 7.06 and p <0.05; the unadjusted recalculation reports an odds ratio of 6.727 and p = 0.052. They answer related but not necessarily identical statistical questions. The reported intervals also differ slightly. The registry record does not provide enough detail to determine the reasons for every difference.

How should p-values be read?

A p-value assesses how compatible the observed data are with a specified null model under the assumptions of the analysis. It does not measure the probability that a hypothesis is true, the size of an effect, or the practical importance of a result. The recalculated unadjusted p-value is 0.052. The registry reports p <0.05 from its logistic regression analysis. Because these results come from different analyses, they should be described separately. A p-value near a conventional threshold does not remove the uncertainty represented by the confidence intervals.

What does randomization contribute?

In general, random allocation is intended to make intervention groups comparable in expectation with respect to measured and unmeasured baseline characteristics. Randomization does not ensure that groups are identical in a particular trial, especially when the outcome counts are limited. Interpretation also depends on how participants were analyzed, whether outcomes were observed, and how deviations from assigned care were handled. The registry says both intent-to-treat and per-protocol populations were analyzed but reports the per-protocol results. The allocation sequence and concealment procedures are not reported in the registry record.

Why does over-dispersion matter?

Over-dispersion is a general concern for count outcomes when variability exceeds what a chosen model expects. It can make model-based standard errors too small if ignored. The primary outcome in this record is a count of participants with a binary event, and the posted comparison uses group counts and proportions, with a logistic regression analysis reported by the registry. No over-dispersion assessment is reported in the registry record. The issue should not be presumed to apply; it is a general model-checking consideration rather than a finding about this trial.

The registry identifies the reported analysis as a superiority analysis, but does not report the full statistical analysis plan, the model covariates, or whether any interim analyses took place. Those details are not reported in the registry record. Accordingly, the posted results support a descriptive comparison of the recorded endpoint and an estimate of its uncertainty, while leaving some analysis decisions unavailable for independent evaluation.

10. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is pinned down by the observed data. A confidence interval gives a range of values compatible with the data and the method used, under the assumptions of that method. It is not a range containing a fixed proportion of individual outcomes, and it does not mean that every value inside the interval is equally plausible.

For the recalculated risk difference of 0.128, the 95% confidence interval runs from 0.003 to 0.252. The interval spans a broad range of absolute group differences, so the point estimate alone gives an incomplete account of uncertainty. The recalculated odds ratio is 6.727, with a 95% confidence interval from 0.769 to 58.82. The registry’s logistic regression odds ratio is 7.06, with a 95% confidence interval from 0.8 to 62.2. The recalculated risk ratio is 5.846, with a 95% confidence interval from 0.738 to 46.3. These relative-measure intervals are also broad.

The limited number of recorded initiation events is relevant to this uncertainty: the posted counts are 1 in CDC-PrEP and 6 in SBCM-PrEP. Estimates based on limited events can vary considerably with a small change in the observed data. The confidence intervals reflect that limited precision; they should not be read as evidence that the point estimate is known exactly.

The recalculated intervals and the registry’s interval arise from different analysis approaches. The recalculated results are unadjusted calculations from the posted summaries; the registry reports a logistic regression analysis. The registry record does not provide enough model detail to explain the full relationship between those estimates. Both sources of uncertainty should be considered when reading the outcome, along with the fact that the reported population is per protocol.

Statistical precision is not the same as clinical or practical importance. The registry record does not report a threshold for a meaningful difference in initiation, so the confidence intervals cannot be classified against such a threshold. The results indicate an uncertain estimated contrast in documented initiation rather than a precise estimate of what would occur in another population or service setting.

11. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not a record of the original trial’s design calculation. Its rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Its columns describe participants per arm for 80% power and participants per arm for 90% power. These are per-arm participant counts, not total event counts.

In plain terms, the 80% power column gives the illustrative number of participants needed in each group for a design to have an 80% chance of detecting the effect used in that row, if the stated planning assumptions hold. The 90% power column gives the corresponding per-arm planning count for a higher chance of detecting that effect. These are prospective design illustrations, not guarantees about a future study’s result. For a given power target, planning to detect a smaller fraction of the observed effect requires more participants than planning to detect the full observed effect.

The listed 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 the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record. The registry enrollment entry is 80, but the planning illustration should not be read as evidence that the original enrollment decision used these recalculated assumptions.

These figures are not observed power. They are planning illustrations computed from the observed effect under the stated assumptions. Because the observed effect is uncertain, planning directly from it can be sensitive to the point estimate; considering smaller effects is a way to see how planning requirements change under a more modest target. The curve should be read in the same planning context, not as a display of realized power or proof that a particular sample size would produce a particular finding.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.026; treatment proportion p₁ = 0.154; average p̄ = 0.090.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4049 = 0.7936.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3947 = 0.3322.
4. n = (0.7936 + 0.3322)² / (0.1275)² = 77.9, rounded up to 78 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 <- 0.0263157894736842                          # control proportion
p1 <- 0.153846153846154                          # 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(5037513)
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 = 78 (80% power), 104 (90% power)
 75% of observed effect: n per arm = 117 (80% power), 156 (90% power)
 50% of observed effect: n per arm = 211 (80% power), 282 (90% power)
power.prop.test: 77.9 
Simulated power at n = 78 per arm: 0.853 (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.

13. Analyses Reported by the Sponsor

The registry reports a logistic regression analysis with an odds ratio of 7.06, a 95% confidence interval from 0.8 to 62.2, and p <0.05. It labels the analysis as superiority. Separately, the unadjusted recalculation from the posted group summaries gives an odds ratio of 6.727, a 95% confidence interval from 0.769 to 58.82, and p = 0.052. The recalculated risk difference is 0.128, with a 95% confidence interval from 0.003 to 0.252.

The sponsor’s reported result and the recalculation are related but not identical analyses. The recalculation is unadjusted and based on the posted event counts and group sizes; the registry identifies logistic regression for its own analysis. The registry record does not report the full model specification or enough detail to reconstruct that analysis. The estimated odds ratios are close in magnitude, but their confidence intervals and reported p-values should be attributed to their respective analyses rather than blended together.

The registry’s confidence interval for the odds ratio includes 1, while its reported p-value is p <0.05. The unadjusted recalculated p-value is 0.052. These results warrant careful reporting without treating a threshold label as a substitute for the estimate and its uncertainty. The discrepancy flag is false, but that does not make the two approaches interchangeable or resolve the need to read the registry analysis and unadjusted recalculation separately.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures and reports two analyses, while identifying intervention engagement and intervention satisfaction as secondary outcomes. It does not report whether the primary and secondary outcomes were handled under a prespecified multiplicity strategy, such as adjustment of significance thresholds or a hierarchy of hypotheses. It is therefore not possible to determine from the registry record whether or how the possibility of multiple statistical comparisons was addressed.

Multiplicity matters because testing several outcomes or contrasts can increase the chance of at least one result appearing notable by chance. This is a general statistical consideration, not a claim that the reported initiation result is or is not a false positive. The registry’s superiority label and reported p-value should be understood in the context of the analysis information available; they do not establish how other comparisons were treated.

The record states that intent-to-treat and per-protocol populations were analyzed, and that the per-protocol results are reported. It defines the per-protocol population as including participants with any exposure to their respective interventions. The primary result therefore does not represent the intent-to-treat population in the posted comparison. The intent-to-treat outcome estimates and their uncertainty are not reported in the registry record.

The registry record does not describe how missing primary outcome data were handled, whether every participant had endpoint ascertainment, or whether any imputation or sensitivity analyses were performed. It also does not report the number of participants excluded from the per-protocol analysis or the reasons for any exclusions. The outcome group sizes are listed as 38 for CDC-PrEP and 39 for SBCM-PrEP, but the available record does not explain how those analysis counts relate to all randomized participants beyond the stated per-protocol definition.

Without details on missingness and analysis population flow, it is not possible to assess whether missing endpoint information or per-protocol selection may have influenced the estimate. The record also does not report the full statistical analysis plan, including the prespecification of outcomes, model covariates, or handling of protocol deviations. These details are not reported in the registry record and should not be inferred from the posted p-value or analysis label.

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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: death (2.4%).

The registry lists serious adverse event information by group. For CDC-PrEP, it records 0 serious adverse events among 39 at risk and 0 deaths. For SBCM-PrEP, it records 1 serious adverse event among 41 at risk and 1 death. The top serious adverse event term is listed as Death, with 2.4% shown in the record.

These safety figures are counts reported in the registry, not estimates of comparative risk with an uncertainty analysis. The record does not state whether the death was judged related to the intervention, nor does it provide enough context to assess its circumstances or cause. The listed event should not be attributed to either intervention based on these figures alone.

The serious-adverse-event denominators differ from the primary per-protocol outcome group sizes. The registry does not explain this difference in the available record. The safety counts should therefore be read within their own reported risk denominators, not combined with or substituted for the primary outcome counts. The absence of a recorded serious adverse event in a group is not proof that no adverse effects occurred; these figures refer specifically to the serious adverse event information posted in the registry.

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

The posted data show more participants with documented PrEP initiation in the SBCM-PrEP group than in the CDC-PrEP group within the reported per-protocol analysis: 6 compared with 1 at 3 months post-baseline. The recalculated absolute difference is 0.128, and the registry’s logistic regression reports an odds ratio of 7.06. These are estimates from the recorded outcome and study population; they are not a guarantee of the same contrast in other settings.

The estimates are imprecise. The risk-difference confidence interval extends from 0.003 to 0.252, and the reported and recalculated odds-ratio intervals are broad. The small event counts mean the result is sensitive to limited information. The registry reports p <0.05 for its logistic regression, whereas the unadjusted recalculation gives p = 0.052. Those values belong to different analyses and should not be collapsed into a single claim.

The endpoint records a dispensed PrEP prescription, not continued use, adherence, or prevention of HIV. The registry’s stated aim includes feasibility, acceptability, and preliminary efficacy, but the primary outcome alone does not answer every part of that aim. The record lists engagement and satisfaction as secondary outcomes; their results are not described in the registry record for this analysis.

The population used for the posted primary result is per protocol, defined as participants with any exposure to their respective intervention. Although the registry says intent-to-treat and per-protocol populations were analyzed, intent-to-treat results are not reported in the registry record. Missing data handling and some analysis details are also not reported. These features limit how far the comparison can be interpreted.

Overall, the results describe a difference in documented initiation in this study, with substantial uncertainty about its size. They do not establish what would happen in other populations or service systems, and they do not establish longer-term PrEP use or HIV outcomes. Neither the point estimate nor a p-value should be treated as a standalone conclusion about the broader effectiveness of either approach.

17. Why This Trial Matters Statistically

This trial raises statistical issues that often arise when evaluating behavioral interventions with a binary clinical-service outcome. Initiation is recorded as a participant-level event, and the observed event counts are limited: 1 in CDC-PrEP and 6 in SBCM-PrEP. In this setting, the point estimate can look large while remaining uncertain. Reporting the absolute risk difference alongside relative measures helps readers see both the group contrast and the scale of the uncertainty.

The analysis also illustrates why a registry’s model-based result and a simple unadjusted recalculation should be identified separately. The logistic regression odds ratio is 7.06, while the unadjusted recalculated odds ratio is 6.727. Their confidence intervals are broad, and the registry-reported p-value differs from the unadjusted p-value. Clear attribution matters: different methods may answer related questions but do not become interchangeable merely because they use the same endpoint.

The per-protocol population is another important issue. The record says both intent-to-treat and per-protocol analyses were conducted, but only the per-protocol result is reported. Because the per-protocol definition depends on exposure to the intervention, the result addresses that analysis population rather than everyone randomized. Without the intent-to-treat estimate and information about missing outcomes, readers cannot assess how the analysis population affects the comparison.

Finally, the sample-size illustration is useful only as a planning exercise based on the observed estimate and stated assumptions. It is not the original design calculation and is not observed power. The trial’s original design assumptions, multiplicity approach, and full analysis plan are not reported in the registry record. These limitations reinforce the value of interpreting the estimate, confidence interval, analysis population, and registry reporting together rather than relying on any single statistic.

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 primary outcome results are reported for the per-protocol population, defined as participants with any exposure to their assigned intervention. Although the registry says it analyzed both intent-to-treat and per-protocol populations, the intent-to-treat results are not reported in the registry record. This limits evaluation of the result for all randomized participants and prevents direct comparison of the two analysis populations.

The event counts are limited, and the confidence intervals are broad. As a result, the magnitude of the group contrast is uncertain. The record reports a logistic regression odds ratio, but does not report the model specification, covariates, or details needed to reconstruct the analysis. The unadjusted recalculation is therefore informative as a separate summary-based analysis, but it cannot substitute for the registry’s full model analysis.

The registry record does not report how missing endpoint data were handled, whether outcome assessment was complete, or how participants who did not receive their assigned intervention were treated in each analysis. It also does not describe the allocation sequence or concealment procedures. Because the study was not masked, the record’s open-label design may be relevant when interpreting behavioral outcomes and outcome ascertainment, although the endpoint is defined as documented prescription dispensing.

The original sample-size justification and design assumptions are not reported in the registry record. The available planning illustration uses the observed effect and stated assumptions, so it should not be used to infer the rationale for the trial’s enrollment. The multiplicity strategy, interim analyses, and full statistical analysis plan are also not reported in the registry record.

The primary endpoint captures documented initiation at 3 months post-baseline. It does not measure persistence, adherence, or subsequent HIV outcomes. The registry identifies intervention engagement and satisfaction as secondary outcomes, but their results are not reported in the registry record. The record also provides a serious adverse event count and a death, but does not state whether the death was related to an intervention. These reporting limits constrain conclusions about both efficacy and safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Integrated PrEP Interventions for People Who Inject Drugs in Rural Kentucky — NCT05037513.
• Registry record last updated 2025-03-20; status last verified 2025-03.
• Results first posted 2025-03-20.
• 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, unmasked behavioral study comparing CDC-PrEP with SBCM-PrEP for people who inject drugs in rural Kentucky. Enrollment is listed as 80. The primary outcome is the number of participants with documented PrEP initiation, measured by a dispensed PrEP prescription at 3 months post-baseline.

The posted per-protocol counts are 1 of 38 for CDC-PrEP and 6 of 39 for SBCM-PrEP. The recalculated risk difference is 0.128, with a 95% confidence interval from 0.003 to 0.252. The registry reports a logistic regression odds ratio of 7.06, with a 95% confidence interval from 0.8 to 62.2 and p <0.05. The unadjusted recalculated p-value is 0.052.

The estimates are imprecise, and the record does not report several details needed to evaluate the full analysis, including missing-data handling, the original sample-size rationale, and the multiplicity approach. The results describe documented initiation in the reported per-protocol population, not longer-term PrEP use or HIV outcomes.