A Study Evaluating Implementation Strategies for the Delivery of APRETUDE for Black cis-and Transgender Women in United States EHE Territories: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Evaluating Implementation Strategies for the Delivery of APRETUDE for Black cis-and Transgender Women in United States EHE Territories (NCT05514509), a randomized phase 4 study. The primary outcome is Mean Intervention Appropriateness Measure (IAM) Score Assessed for SSPs at Month 12.

2. Clinical Question

3. Trial Design

NCT05514509 is a completed phase 4 randomized, open-label, parallel study sponsored by ViiV Healthcare. The registry lists a start date of 2022-10-28 and a primary completion date of 2025-09-02. Enrollment is listed as 295. The study evaluates implementation strategies for delivering cabotegravir (CAB) as HIV pre-exposure prophylaxis across clinical settings for adult Black cisgender and transgender women without HIV infection living in United States Ending the Epidemic (EHE) territories. The registry lists HIV infections as the condition.

There are three implementation arms. SI used standard toolkits and implementation monitoring. EI added enhanced supports, including discussion and informational tools and provider education. ECI combined standard toolkits with enhanced supports such as a sexual health assessment, provider education, videos, informational tools, persistence support, and peer ambassadors. In all arms, the supports were described as available for use as needed. The comparison is therefore among implementation packages, not simply among drug products: cabotegravir delivery is the context, while the strategy for supporting delivery differs.

The registry distinguishes patient study participants, who received commercially available CAB PrEP by prescription from a PrEP provider, from staff study participants involved in offering and administering PrEP at clinical sites. The primary endpoint is a staff measure; several secondary outcomes concern participant initiation or continuation. These endpoint populations are not interchangeable. The overall enrollment figure should not be read as the denominator for every posted result.

Masking is listed as none. The open-label design means participants and relevant study personnel were not masked to the implementation approach. The registry record does not report the trial's original sample-size justification, detailed statistical analysis plan, interim analyses, or a reported inferential analysis for the primary endpoint. The posted comparisons between arm summaries are unadjusted recalculations and should be read as descriptive statistical comparisons, not as a substitute for any sponsor analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 1. SSPs provided input through surveys and interviews. 2. Baseline characteristics and adverse events for SSPs were not collected as it was not required per study design. 3. Semi-structured interviews allowed participants to discuss topics voluntarily and did not require responses on all interview topics.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on the SSPs who completed at least one implementation science questionnaire (ISQ) at any time point. Only those participants with data available for the IAM score at Month 12 were included in this outcome measure.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Baseline characteristics for SSPs were not collected as it was not required as per study design.

6. Primary Endpoint

The registry lists the primary outcome as Mean Intervention Appropriateness Measure (IAM) Score Assessed for SSPs at Month 12, measured over At Month 12.

The primary endpoint is the mean Intervention Appropriateness Measure (IAM) score among SSPs at month 12. The IAM asks whether APRETUDE seems fitting, suitable, applicable, and like a good match for Black women at the respondent's clinic or practice. Each item uses a five-point rating scale from 1, completely disagree, through 5, completely agree. The mean score ranges from 1 to 5, with higher scores indicating greater perceived appropriateness. The measure is intended to capture an implementation outcome: whether staff consider the delivery approach appropriate in their setting.

The registry's analysis population includes SSPs who completed at least one implementation science questionnaire at any time point, while this endpoint includes only those with month 12 IAM data. Month 12 is the stated assessment time; for SSPs assessing PSPs receiving an optional oral lead-in, the registry equates this with month 13. The posted arm summaries are means with standard deviations. A mean provides a compact description of the average rating, while the standard deviation describes variation among the scores contributing to that mean.

This endpoint is useful because implementation depends in part on whether staff regard an approach as fitting their clinic's work and population. It does not measure participant adherence, HIV incidence, or the clinical effectiveness of CAB PrEP. Nor does a high mean by itself establish that a strategy is feasible, acceptable, adopted, or delivered with fidelity. Those are related implementation concepts, but they require their own measures and interpretation.

7. Results Posted in the Registry

• EI - SSP: mean 4.70 versus 4.40 on control; difference 0.30 (95% CI -0.09 to 0.69), standardized effect d = 0.41; z-test p = 0.135.
• ECI - SSP: mean 4.30 versus 4.40 on control; difference -0.10 (95% CI -0.52 to 0.32), standardized effect d = -0.13; z-test p = 0.641.

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.

Number of Black Women (Both Cis- and Trans) Who Initiate APRETUDE by Study Arm

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • EI - PSP: 11.6% (10/86) versus 8.4% (13/154) on control; risk difference 3.2 percentage points (95% CI -4.9 to 11.3), risk ratio 1.38 (0.63–3.01); unadjusted two-proportion z-test p = 0.421.
  • ECI - PSP: 2.0% (6/296) versus 8.4% (13/154) on control; risk difference -6.4 percentage points (95% CI -11.1 to -1.7), risk ratio 0.24 (0.09–0.62); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EI - PSP and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for ECI - PSP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Black Women (Both Cis- and Trans) Who Initiate APRETUDE by Clinic Setting

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Primary Care Clinic - PSP: 3.0% (10/336) versus 4.9% (4/81) on control; risk difference -2.0 percentage points (95% CI -7.0 to 3.1), risk ratio 0.60 (0.19–1.87); unadjusted two-proportion z-test p = 0.379.
  • HIV Specialist Clinic - PSP: 12.6% (15/119) versus 4.9% (4/81) on control; risk difference 7.7 percentage points (95% CI 0.1 to 15.3), risk ratio 2.55 (0.88–7.41); unadjusted two-proportion z-test p = 0.069.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Primary Care Clinic - PSP 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 HIV Specialist Clinic - PSP and the control. The interval gives the range of effects that remain compatible with the data.

Number of Black Women (Both Cis and Trans) Who Continue APRETUDE Beyond a First Dose by Study Arm

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • EI - PSP: 3.0% (10/336) versus 20.8% (32/154) on control; risk difference -17.8 percentage points (95% CI -24.5 to -11.1), risk ratio 0.14 (0.07–0.28); unadjusted two-proportion z-test p = <0.001.
  • ECI - PSP: 7.4% (22/296) versus 20.8% (32/154) on control; risk difference -13.3 percentage points (95% CI -20.4 to -6.3), risk ratio 0.36 (0.22–0.59); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for EI - PSP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for ECI - PSP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the implementation picture beyond staff ratings of appropriateness. They include counts of PSPs who initiated APRETUDE by study arm and clinic setting, counts who continued beyond a first dose, and staff questionnaire measures addressing appropriateness and staffing sufficiency at different assessments. Together, these endpoints address uptake and aspects of the implementation process, while the primary IAM endpoint captures staff perceptions of fit at month 12.

The pattern across posted results is not a single uniform signal across every outcome. Initiation and continuation are distinct: beginning APRETUDE does not necessarily indicate ongoing use beyond a first dose. Clinic setting comparisons are also not interchangeable with randomized study-arm comparisons. Differences between settings may reflect context and composition as well as implementation, and the registry summaries do not establish that a setting caused a difference. The primary staff measure and PSP outcomes have different respondents, definitions, and analysis populations, so apparent alignment or divergence should be interpreted as complementary description rather than a direct consistency test.

The record lists a large number of outcome measures, while no reported analyses are listed for the secondary endpoints. The recalculated comparisons are unadjusted and therefore do not account for testing multiple endpoints and contrasts. When many comparisons are considered, some estimates may look notable by chance even if there is no underlying difference. Without a reported hierarchy of endpoints, multiplicity adjustment, or full analysis plan, isolated p-values deserve less weight than a prespecified primary analysis.

Secondary results can help identify patterns that merit further study, but they do not replace the primary endpoint or establish an overall implementation effect. Interpretation should consider confidence intervals, denominators, the endpoint's definition, and whether the comparison follows randomized assignment or contrasts other groupings such as clinic settings. The registry record does not report enough analysis detail to establish how missingness, clustering, or repeated assessments were handled across the secondary outcomes.

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

• Mean IAM Score Assessed for SSPs Over Time
• Change From Baseline in IAM Score Assessed for SSPs
• Number of SSPs With Responses to Appropriateness of APRETUDE Assessed by Implementation Science Questionnaire (ISQs) at Baseline
• Number of SSPs With Responses to Appropriateness of APRETUDE Assessed by ISQs at Month 4
• Number of SSPs With Responses to Appropriateness of APRETUDE Assessed by ISQs at Month 12
• Number of SSPs With Responses to APRETUDE Staffing Sufficiency Assessed by ISQs at Months 4 and 12
• Number of SSPs With Responses to Appropriateness of APRETUDE Assessed by Semi-structured Interview (SSI) at Month 4
• Number of SSPs With Responses to Appropriateness of APRETUDE Assessed by SSI at Month 12

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean describe?

A mean is the arithmetic average of the observed IAM scores in an arm. Since the IAM score ranges from 1 to 5, the arm mean describes the average staff rating on that scale. It is not the proportion of staff who agreed, nor does it show how many respondents selected any particular answer. Different score distributions can have the same mean. The standard deviation adds information about dispersion: a smaller standard deviation indicates scores clustered more closely around the mean, while a larger one indicates greater variation. It is not the uncertainty interval for the mean.

What does a mean difference compare?

The posted contrasts compare each enhanced implementation arm with SI. The mean difference is the enhanced arm mean minus the SI mean. A positive estimate indicates a higher average score in the enhanced arm; a negative estimate indicates a lower average. The estimate is calculated from posted summary statistics and is unadjusted. It does not account for other variables, site structure, repeated measurements, or a more complex design unless those adjustments are explicitly part of the calculation; such adjusted modeling is not reported in the registry record.

The posted comparison also gives a pooled standard deviation and a standardized effect estimate. A pooled standard deviation combines the arm-level variability for purposes of expressing the difference relative to the observed spread. A standardized effect can make a mean contrast easier to compare across scales, but it does not replace the original scale difference or its uncertainty. These are recalculated descriptions, not reported sponsor model estimates.

How should the confidence interval be read?

A confidence interval expresses the range of values reasonably compatible with the data under the calculation's assumptions. For a mean difference, an interval that crosses zero includes no difference as one value compatible with the observed data. An interval wholly above or below zero would indicate the estimated contrast is more clearly directional under that calculation. A confidence interval is not a guarantee that the true value lies within the particular interval, and it does not measure the probability that a hypothesis is true.

The posted p-values are unadjusted. A p-value describes how unusual the data, or data more extreme, would be under a specified null model; it is not the probability that the null hypothesis is true, nor a measure of clinical or implementation importance. The registry record does not report the sponsor's primary inferential analysis. Accordingly, the recalculated p-values and intervals should not be mistaken for a complete analysis plan or for adjusted trial findings.

Why does the analysis population matter?

The primary endpoint is based on SSPs with month 12 IAM data, within the broader description of SSPs who completed at least one implementation science questionnaire. Availability of endpoint data can affect which respondents contribute to a mean. The registry record does not report how missing month 12 scores were handled beyond defining the endpoint population, nor does it report a missing-data sensitivity analysis. The primary summaries therefore describe participants with available endpoint data and cannot alone establish whether missingness changed the result.

Other outcomes use PSPs and have their own denominators. Staff and patient outcomes answer different questions and should not be combined. The arm-level counts in one endpoint also should not be assumed to be the same analysis population as another endpoint simply because both refer to the same implementation arm.

What is the role of randomization and masking?

Random allocation is intended to support comparable groups at the point of assignment, reducing systematic differences in expectation. It does not guarantee balance in every characteristic, particularly in finite samples. The study is open-label, so knowledge of the assigned implementation approach may influence perceptions, reported questionnaire responses, or delivery behavior. These considerations are relevant to interpretation of a staff-reported appropriateness measure. The registry record does not report details needed to assess concealment of assignment, site-level allocation procedures, or adjustments for clustering.

Finally, the study has multiple outcomes and comparisons. When many hypotheses are examined, the chance of at least one apparently notable result can increase. Whether and how the investigators controlled that risk is not reported in the registry record. Thus the unadjusted secondary comparisons carry less evidential weight than a prespecified, fully reported analysis with a documented multiplicity strategy.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate an estimated effect. For the primary EI-versus-SI contrast, the estimated mean difference is 0.3 and its 95% confidence interval runs from -0.094 to 0.694. This interval includes zero and spans values consistent with a lower EI mean as well as a higher one. For ECI versus SI, the estimate is -0.1 and the interval is -0.520 to 0.321, also including zero. The estimates therefore have uncertainty in both directions relative to no mean difference.

The interval width is influenced by the amount of score variation and the number of observations contributing to the arm means. The reported standard deviations differ across the arms, and the primary analysis counts range from 26.0 to 32.0. These quantities help explain why a point estimate should not be read in isolation. The standard deviations describe variation in individual IAM scores; the confidence intervals describe uncertainty around the comparative mean differences. They answer different questions.

Intervals that include zero do not establish equivalence or rule out an important difference. An equivalence conclusion requires a prespecified margin and an analysis designed for that question; such a margin and analysis are not reported in the registry record. Conversely, statistical uncertainty does not imply that the arms are identical. It means the posted summaries do not locate the mean contrast precisely enough to distinguish its direction from zero using these unadjusted calculations.

The intervals are recalculated from posted summary statistics and should be treated as unadjusted. The registry record does not report a sponsor analysis for the primary comparisons or a model accounting for features such as site clustering. If the sponsor's own analysis becomes available, it takes precedence over these recalculations. Practical relevance also depends on how much change in IAM score would matter to staff and implementation; a threshold for a meaningful difference is not reported in the registry record.

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 describe hypothetical sample sizes for detecting effects based on the observed comparisons; they are not the trial's original design targets. For these continuous IAM comparisons, the entries are participants per arm, not total participants or total events. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial's original sample-size planning.

The 80% power column gives the estimated participants per arm under those assumptions for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding per-arm planning estimate for a 90% chance. These are design calculations, not probabilities that the observed findings are correct, and they do not say whether the completed study had adequate power for its actual outcomes.

For EI versus SI, planning for 100% of the observed effect gives 92 participants per arm for 80% power and 123 for 90% power. Planning for 75% gives 163 and 218; planning for 50% gives 367 and 491. For ECI versus SI, the corresponding figures are 982 and 1,314 for 100%, 1,745 and 2,336 for 75%, and 3,926 and 5,256 for 50%. The larger requirements for smaller target effects illustrate the general principle that detecting a subtler difference usually requires more participants, all else equal.

These figures are planning illustrations only, not observed power. They rely on the stated assumptions and the observed effect estimates, which may themselves be uncertain. They should not be interpreted as the sample sizes actually assigned in the trial or as evidence that the study did or did not achieve a particular power.

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 = 0.300; pooled standard deviation σ = 0.725.
2. n = 2 × (1.96 + 0.842)² × 0.725² / 0.300² = 91.6, rounded up to 92 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 <- 0.3                      # observed difference in means
sigma <- 0.724603339765971                     # 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(5514509)
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 = 92 (80% power), 123 (90% power)
 75% of observed effect: n per arm = 163 (80% power), 218 (90% power)
 50% of observed effect: n per arm = 367 (80% power), 491 (90% power)
power.t.test: 92.5 
Simulated power at n = 92 per arm: 0.797 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists many outcome measures, including multiple staff questionnaire assessments, participant initiation and continuation outcomes, and comparisons across implementation arms or clinic settings. Examining many endpoints increases the chance that one or more results may appear statistically notable by chance. The registry record does not report a multiplicity strategy, such as a prespecified hierarchy, family-wise error adjustment, or false-discovery procedure. The unadjusted p-values should therefore be treated as exploratory rather than as confirmatory evidence across the full set of outcomes.

The record reports no analyses in the reported-analysis listing. It does not provide a detailed statistical analysis plan, specify which secondary analyses were prespecified, or describe interim analyses. The primary result summaries and recalculated comparisons can be interpreted descriptively, but they do not show whether the sponsor used additional adjustment, model structure, or sensitivity analyses. Those details are not reported in the registry record.

Missing data are relevant because the primary endpoint includes only SSPs with month 12 IAM scores, after defining the broader eligible staff group as those who completed at least one questionnaire at any time point. This is a complete-case endpoint summary for the available month 12 scores, based on the stated population definition. The registry record does not report the number or characteristics of staff missing month 12 scores, reasons for missingness, imputation methods, or sensitivity analyses. It is therefore not possible to assess from the posted endpoint description whether missingness could have influenced the mean ratings.

Different endpoints have different populations and denominators, including staff and patient participants. A denominator for one endpoint should not be carried over to another. The registry record does not report how site clustering was addressed, whether all randomized participants were analyzed in their assigned arms for each outcome, or how deviations from implementation assignment were handled. The exact analysis populations and handling of missing data for all secondary measures are not reported in the registry record.

Randomization supports comparisons between assigned groups, but open-label delivery, site-level implementation, incomplete outcome data, and multiple comparisons can complicate interpretation. These limitations do not invalidate the posted summaries; they define what can reasonably be concluded from them. A full analysis plan and sponsor-reported results would be needed to assess whether the posted unadjusted calculations agree with the intended inferential approach.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: back pain (2.3%), dysarthria (2.3%), hypoaesthesia (2.3%), presyncope (2.3%), abortion spontaneous (1.8%).

The registry reports serious adverse event figures for PSPs by implementation arm, with 1 serious event among 56 at risk in SI, 0 among 63 in EI, and 1 among 44 in ECI. Deaths are reported as 0 in each arm. These are counts within the stated at-risk groups. The figures describe serious adverse events recorded in the study; they do not by themselves establish whether an event was caused by APRETUDE, the implementation strategy, or another factor.

The listed serious-event terms include Back pain, Dysarthria, Hypoaesthesia, and Presyncope, each reported at 2.3%, and Abortion spontaneous at 1.8%. These terms and percentages should be interpreted in the context of the registry's adverse event reporting, rather than as comparative risk estimates between arms. The record excerpt does not provide event-level timing, exposure duration, causal assessments, or detail needed to compare event patterns reliably.

Small event counts can be unstable and should not be treated as evidence that an arm has no safety risk. The registry record does not report enough information to characterize the overall safety profile or attribute events to a particular component of the study.

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

The primary result describes how staff who posted month 12 IAM data rated the appropriateness of APRETUDE for Black women at their clinics or practices. Mean scores were 4.4 in SI, 4.7 in EI, and 4.3 in ECI on a scale from 1 to 5. The unadjusted comparisons with SI have confidence intervals that include zero. The data therefore give a descriptive picture of staff ratings, but the contrasts do not precisely establish a difference in either direction.

This finding does not establish that EI or ECI is equivalent to SI. Demonstrating equivalence requires a defined margin and an appropriate design and analysis, neither of which is reported in the registry record. Nor does a lack of a clear difference establish that implementation strategy is irrelevant. The result may reflect uncertainty, the available endpoint data, variation among staff, or other factors that cannot be distinguished from these summary statistics alone.

The endpoint is not a measure of whether cabotegravir prevents HIV infection, and it does not establish clinical benefit or harm. It measures staff perceptions of appropriateness. Participant initiation and continuation outcomes speak to different aspects of implementation, but they are not substitutes for HIV-related clinical outcomes. The posted secondary contrasts are unadjusted and should not be treated as definitive evidence that one approach caused more or less uptake or persistence.

Randomization is an important design feature, but the open-label nature of the study means knowledge of the strategy could affect staff responses or behavior. The primary endpoint also relies on data available at month 12, and missing-data methods are not reported in the registry record. The reported means and recalculated intervals cannot address these concerns fully.

In practical terms, the registry record documents a comparison of three implementation approaches and reports staff appropriateness ratings alongside additional implementation measures. It does not provide a sponsor-reported inferential analysis or enough detail to make strong claims about strategy effectiveness, mechanisms, or generalizability beyond the studied settings and populations. The statistical interpretation should remain tied to the specific measures and populations that were assessed.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it places an implementation outcome, staff-rated appropriateness, at the center of a randomized comparison. Clinical trials often emphasize patient-level outcomes, while successful delivery also depends on how services fit local practice. Measuring staff perceptions can help describe that context, but it requires careful distinction from clinical efficacy and patient experience. The separate staff and patient populations in the registry make that distinction particularly important.

The three-arm structure compares standard implementation with two approaches that add supports. This can inform questions about how implementation support is organized, while the open-label design reflects that the strategies are visible and operational in clinical settings. Those characteristics also bring analytical challenges: staff ratings may be influenced by awareness of the approach, and participants are situated within clinical sites where responses may be correlated. The registry record does not report whether site clustering was modeled.

The primary mean differences are modest in numerical direction and have intervals spanning zero. This illustrates why point estimates, uncertainty intervals, and the endpoint's meaning need to be considered together. The secondary outcomes add dimensions of uptake and continuation, but their unadjusted nature and the absence of a reported analysis plan limit confirmatory interpretation. More outcomes do not automatically create more certainty.

The record also highlights the difference between a trial's enrollment figure and endpoint-specific analysis populations. Staff questionnaire results and patient initiation outcomes have different denominators and answer different questions. Clear reporting of populations, missingness, analysis procedures, and multiplicity is essential when communicating implementation evidence. These features shape how readers judge precision and the scope of conclusions, even when the central result is easy to state.

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.

Several limitations specific to this record constrain interpretation. The primary outcome is a staff-reported appropriateness score, so it captures perceptions rather than directly observed implementation fidelity or a patient clinical endpoint. The open-label design may influence responses because staff knew which implementation supports were available. The registry record does not report a blinding or independent outcome-assessment process that would address this concern.

The primary endpoint is limited to SSPs with month 12 IAM data. The record does not report missingness counts, reasons for missing data, or sensitivity analyses, so the effect of incomplete questionnaire data cannot be assessed. It also does not report the detailed statistical plan, sponsor-reported primary analysis, interim analyses, or a multiplicity procedure. The recalculated arm comparisons are unadjusted and should not be treated as a complete substitute for those analyses.

Implementation occurs in clinical settings, but the registry record does not report whether statistical methods accounted for clustering by site or differences in site characteristics. Randomization is listed, but assignment procedures and any analysis adjustments are not reported. Consequently, the posted summary comparisons cannot establish how much variation is attributable to individual responses versus clinic context.

The listed overall enrollment and outcome-specific denominators refer to different groups and measures. This makes it important not to infer a common analysis population across endpoints. Secondary outcomes also involve different populations and definitions, including initiation, continuation, and clinic setting. Their unadjusted comparisons may be affected by multiple testing and should not be treated as equally strong evidence.

Finally, the study is situated in United States EHE territories and concerns Black cisgender and transgender women and their clinical settings. The extent to which the results apply to other populations, locations, service systems, or PrEP delivery approaches is not reported in the registry record. These limitations define the boundaries of interpretation rather than negating the descriptive value of the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study Evaluating Implementation Strategies for the Delivery of APRETUDE for Black cis-and Transgender Women in United States EHE Territories — NCT05514509.
• Registry record last updated 2026-10-01; status last verified 2026-09.
• Results first posted 2026-10-01.
• 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

NCT05514509 is a completed, phase 4, randomized, open-label, parallel study of implementation strategies for delivering cabotegravir PrEP to Black cisgender and transgender women in United States EHE territories. The three approaches were Standard Implementation, Enhanced Implementation, and Enhanced Collaborative Implementation. The primary endpoint was the mean month 12 IAM score among SSPs with available endpoint data.

Posted mean IAM scores were 4.4 for SI, 4.7 for EI, and 4.3 for ECI. Recalculated, unadjusted comparisons with SI have confidence intervals that include zero. Additional posted outcomes concern participant initiation and continuation, but they represent different populations and implementation questions. The registry record does not report the sponsor's detailed statistical analysis plan, multiplicity strategy, or a sponsor-reported analysis for these comparisons. The findings are best read as descriptive summaries with uncertainty, not as definitive evidence of clinical effectiveness or strategy equivalence.