Electronic Pre-exposure Prophylaxis (PrEP) Initiation and Maintenance Home Care System: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Electronic Pre-exposure Prophylaxis (PrEP) Initiation and Maintenance Home Care System (NCT03729570), a randomized na study. The primary outcome is Difference in Tenofovir-diphosphate (TFV-DP) Levels Between Intervention and Control Arms at 6 Months Follow-up.

2. Clinical Question

The primary outcome is titled as a difference in TFV-DP levels, but the posted outcome values are counts of participants meeting an adherence-related biomarker definition. The registry describes levels corresponding to more than 4 doses per week as the cutpoint. It gives different TFV-DP thresholds for emtricitabine/tenofovir disoproxil fumarate and emtricitabine/tenofovir alafenamide. The outcome therefore represents a thresholded biomarker measure rather than a comparison of average TFV-DP concentrations.

The posted primary results include 17 of 31 participants in ePrEP and 7 of 26 in standard care meeting the outcome definition. These are the observed biomarker counts at the specified follow-up, not counts of everyone enrolled. Why the outcome denominators differ from total enrollment is not reported in the registry record. The clinical question is thus limited to the recorded biomarker outcome among participants contributing those data.

3. Trial Design

This was a randomized, parallel-group trial with no masking reported. The registry lists the study as completed, with enrollment of 217. The listed start date is 2019-05-28 and the primary completion date is 2022-05-31. The phase is recorded as not applicable. These design features identify the broad structure of the comparison, but do not establish how allocation was generated, concealed, or implemented; those details are not reported in the registry record.

The intervention arm was ePrEP, a home-care system intended to support telemedicine PrEP initiation and continued care. The description names a smartphone application for video consultations with a clinician and secure messaging, but the full intervention description is not available in the registry record. The comparison arm received standard care, including referral to a public website that locates nearby PrEP providers. The record characterizes this as the level of PrEP service access available to members of the general public.

Both arms were assessed using self-collected dried blood spot specimens for the primary biomarker outcome. TFV-DP was measured using liquid chromatography/tandem mass spectrometry. The registry describes the primary follow-up as 6 months and the secondary follow-up as 12 months. For the primary measure, participants were classified using medication-level cutpoints intended to indicate dosing above the stated weekly threshold. The posted results report counts meeting that definition.

Enrollment and outcome denominators should not be treated as interchangeable. The registry records 217 enrolled, while the primary outcome results include 31 ePrEP and 26 standard-care participants. The 12-month results use different arm denominators. Reasons for these differences, including the role of missing specimens, participant withdrawal, or other eligibility rules at each time point, are not reported in the registry record.

The registry gives no original sample-size justification, allocation ratio rationale, or detailed analysis plan. It also does not report how the randomization process was conducted or whether any protocol changes occurred. Those omissions limit assessment of how fully the posted comparison corresponds to the study’s planned design.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants with biomarker data indicating adherent daily PrEP dosing. For participants either reporting the use of both medications in the period or not reporting which medication they used during this period, investigators used decision rules to determine adherence. For instance, if a participant had a TFV-DP level above both cutpoints, they were classified as adherent.

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 Difference in Tenofovir-diphosphate (TFV-DP) Levels Between Intervention and Control Arms at 6 Months Follow-up, measured over 6-month follow up.

The primary endpoint is a count of participants whose TFV-DP biomarker result met the registry’s definition of adherent daily PrEP dosing at 6-month follow-up. Although the endpoint title refers to a difference in TFV-DP levels, the posted result is binary: participants are counted as meeting or not meeting the specified threshold. It is not a comparison of the average biomarker concentration in each arm.

The registry explains that TFV-DP measured from self-collected dried blood spot samples can be interpreted as an indicator of the mean number of days per week PrEP was taken over approximately one month before specimen collection. The primary cutpoint corresponds to more than 4 doses per week. For participants taking emtricitabine/tenofovir disoproxil fumarate, the stated TFV-DP threshold is >1000 femtomole per blood spot; for emtricitabine/tenofovir alafenamide, it is >140 femtomole per blood spot.

A biomarker outcome offers an objective measure related to medication exposure over a recent period, rather than relying only on self-report. It remains a proxy for medication-taking behavior and is tied to the specimen collection and interpretation rules. The registry describes additional decision rules for participants reporting use of both medications or not reporting which medication they used, but the full explanation is incomplete. The endpoint does not, by itself, establish the broader quality, acceptability, or long-term persistence of care.

7. Results Posted in the Registry

• ePrEP: 54.8% (17/31) versus 26.9% (7/26) on control; risk difference 27.9 percentage points (95% CI 3.5 to 52.4), risk ratio 2.04 (1.00–4.14); unadjusted two-proportion z-test p = 0.033.

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.

Difference in Tenofovir-diphosphate (TFV-DP) Levels Between Intervention and Control Arms at 12 Months Follow-up

• 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:
  • ePrEP: 40.5% (15/37) versus 41.7% (20/48) on control; risk difference -1.1 percentage points (95% CI -22.2 to 20.0), risk ratio 0.97 (0.58–1.63); unadjusted two-proportion z-test p = 0.917.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ePrEP and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: the biomarker-based comparison at 12-month follow-up. Its general pattern is less distinct than the primary 6-month comparison: the reported estimate is close to no difference, and its confidence interval includes values in both directions. This endpoint is related to the primary result because both use TFV-DP biomarker data and a threshold-based adherence outcome, but it addresses a later follow-up time and has different outcome denominators.

The secondary result does not formally test whether an observed difference at 6 months changed by 12 months. The registry record does not report a longitudinal model, a direct comparison of time points, or an analysis of persistence over time. Separate cross-sectional comparisons at follow-up cannot establish a within-participant trajectory. The registry also does not report why the participants contributing data differ between time points.

Unadjusted secondary findings generally carry less weight than a primary endpoint because secondary outcomes may be one of several questions considered, and repeated testing can increase the chance of chance-positive findings. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Consequently, the later comparison is best treated as supportive descriptive evidence, not as an independent confirmation or a definitive contradiction of the primary result.

At the same time, lack of a statistically clear secondary difference is not proof that the intervention and comparator are equivalent. The estimate and its uncertainty should be considered together, and the available record does not describe an equivalence margin or a design intended to test equivalence. The secondary outcome adds information about the later measured follow-up, but it cannot resolve the limitations of the primary comparison or explain the difference in observed data availability.

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

• Difference in Tenofovir-diphosphate (TFV-DP) Levels Between Intervention and Control Arms at 12 Months Follow-up

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, each participant is classified according to whether the defined event occurred. In this trial, the posted event is meeting the TFV-DP threshold used to indicate the specified adherence level. The arm results are counts of participants meeting that definition alongside the number contributing to the reported outcome. A count comparison is different from an analysis of continuous TFV-DP concentrations: it depends on the chosen threshold and does not preserve how far a measurement lies above or below it.

What does a risk difference describe?

A risk difference subtracts the event proportion in one arm from the event proportion in the other. Positive values indicate a larger observed event proportion in the arm named in the comparison; negative values indicate a smaller one. For the primary follow-up, the posted estimate is 0.279 for ePrEP relative to standard care. This is an unadjusted contrast based on the posted counts, not a model-adjusted effect. A risk difference is often useful because it expresses the contrast on the probability scale, but its interpretation depends on the outcome definition and the people represented by each denominator.

How should a confidence interval be read?

A confidence interval describes statistical uncertainty around an estimated effect under the method used to construct it. It is not a range guaranteed to contain the true effect, and it does not account automatically for sources of uncertainty omitted by the analysis, such as unaddressed missing data or bias. For the primary risk difference, the interval is entirely on the positive side of no difference. For the 12-month estimate, the interval spans no difference and values on both sides. The width and placement together are more informative than whether a p-value crosses a conventional threshold alone.

What does the p-value contribute?

A p-value summarizes how compatible the observed data are with a specified null model, assuming that model and the analysis assumptions are appropriate. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. The registry posts unadjusted p-values of 0.033 for the primary comparison and 0.917 for the secondary comparison. These values do not replace the estimates, confidence intervals, outcome definitions, or assessment of missingness.

Why are relative measures also sometimes reported?

A relative risk compares event proportions as a ratio, while an odds ratio compares event odds. Both put the contrast on a relative scale, unlike the risk difference. Relative measures can look different from absolute differences, especially when an event is not rare. The registry record includes relative measures for the comparisons, but the main interpretation uses the risk difference because it directly describes the absolute contrast in the proportion meeting the endpoint. The registry does not report an adjusted model for these measures.

Why does the threshold matter?

Turning a measured biomarker into a binary endpoint discards some detail. Two participants on the same side of a cutpoint may have different measured levels, while observations just on opposite sides are classified differently. The threshold is clinically interpretable according to the registry’s dosing description, but it remains a classification rule. The medication-specific thresholds and decision rules matter to interpretation; the full decision-rule description is not reported in the registry record.

What can randomization support?

Random assignment is intended to make treatment groups comparable on average, including for factors not measured by investigators. This supports a between-arm interpretation when allocation is implemented as planned and outcome data and analyses are handled appropriately. The registry identifies the study as randomized, but does not report the sequence-generation method, concealment, baseline balance, or full analysis population. It is therefore not possible from the registry record alone to evaluate those implementation details.

What does over-dispersion mean for these results?

General explanation: over-dispersion arises when observed variability is greater than a statistical model expects. It is a concern in some count-data analyses, where treating events as having a simple Poisson-like variability can make uncertainty appear too small. The posted primary endpoint is a binary participant count, and the registry does not describe an over-dispersion model or report dispersion estimates. Over-dispersion is therefore a general concept rather than a stated feature of this analysis.

The registry reports no formal analyses in its analysis listing, although it posts outcome counts and unadjusted comparisons. The exact test or interval construction used for the posted comparisons is not reported in the registry record. That distinction matters: a statistical explanation of risk differences and confidence intervals describes general interpretation, not an undocumented claim about the precise computational procedure used by investigators.

11. Confidence Intervals and Precision

Precision is reflected in the range of effects compatible with the data under the confidence-interval method. The primary estimate is positive, and its reported interval remains above zero. This supports a directional difference in the posted 6-month comparison under that calculation, but the interval also spans a range of effect sizes. The result is not an exact measure of the underlying contrast, and uncertainty about missing outcome data or analysis choices is not captured merely by the interval.

At 12 months, the interval extends across no difference and permits effects on either side. This indicates less certainty about the direction of the contrast at that follow-up. The p-value of 0.917 is consistent with the absence of a clear distinction in the posted comparison, but does not demonstrate equivalence. Establishing equivalence would require a prespecified margin and an analysis designed to address it; neither is reported in the registry record.

The number of observations contributing to each outcome is important to precision. The primary comparison uses 31 ePrEP and 26 standard-care participants, while the secondary comparison uses 37 and 48, respectively. These denominators are not the total enrollment figure. The reasons they differ and the extent to which missing outcome information could affect the estimates are not reported in the registry record.

Confidence intervals address sampling uncertainty under their assumptions. They do not by themselves account for selection into the observed outcome set, measurement limitations, deviations from the intended intervention, or unreported analytic decisions. Precision should therefore be read alongside the outcome counts and the registry’s reporting gaps, not as a complete measure of reliability.

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 display is a planning illustration derived from the observed effect, not a description of the trial’s original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. The listed calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column represents the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the selected effect under the listed assumptions, if that effect were the true one. The 90% power column uses a higher chance of detection and consequently requires more participants per arm. These are planning concepts: power is the probability of a statistically significant result under a specified true effect and analysis setup, not the probability that a study result is correct.

Rows for a smaller fraction of the observed effect require more participants because smaller contrasts are harder to distinguish from random variation. The displayed numbers are therefore sensitive to the effect chosen as the planning target. The observed effect may not be a stable estimate of the effect expected in a future study, particularly when the original comparison is uncertain. These figures are not observed power.

The same assumptions govern the sample-size curve: it illustrates how planning requirements change with the target effect rather than reporting actual enrollment or an observed trial outcome. It should be used as a design illustration only. It does not establish that the completed study was designed around these targets, and it does not fill in the unreported original design rationale.

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 = 0.269; treatment proportion p₁ = 0.548; average p̄ = 0.409.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6952 = 1.3627.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6666 = 0.5611.
4. n = (1.3627 + 0.5611)² / (0.2792)² = 47.5, rounded up to 48 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 <- 0.269230769230769                          # control proportion
p1 <- 0.548387096774194                          # 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(3729570)
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 = 48 (80% power), 64 (90% power)
 75% of observed effect: n per arm = 83 (80% power), 111 (90% power)
 50% of observed effect: n per arm = 180 (80% power), 240 (90% power)
power.prop.test: 47.5 
Simulated power at n = 48 per arm: 0.806 (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 registry record does not report a multiplicity strategy for the primary and secondary comparisons. It does not say whether a formal hierarchy was prespecified, whether adjustment for multiple testing was planned, or how any adjustment would affect interpretation. The primary result is therefore described using its posted unadjusted comparison; the secondary result should be read with the additional caution that it is not reported as multiplicity-adjusted.

Missing-data handling is also not reported in sufficient detail. Enrollment is listed as 217, but the primary outcome is reported for smaller groups, and the 12-month outcome uses different denominators. The registry does not explain whether these differences arise from missing specimens, withdrawal, medication-use reporting, eligibility for the biomarker interpretation, or other reasons. No imputation method, sensitivity analysis, or missingness assumption is reported in the registry record. It is not possible to determine whether participants without endpoint data differ systematically from those included in the posted counts.

The analysis populations are not described. The record does not state whether results follow an intention-to-treat population, a per-protocol population, or another defined set. It also does not explain how participants were handled if they did not initiate PrEP, changed medication, or had incomplete biomarker information. The primary endpoint description mentions decision rules for some medication-use reporting situations, but the full rules are not available.

These omissions matter because analysis choices can influence both the estimated contrast and its uncertainty. Randomization does not by itself eliminate bias if outcome availability or inclusion in the analysis depends on post-randomization events. The posted counts remain useful descriptions of the observed data, but the registry record does not provide enough detail to evaluate how missingness and population definitions may affect the comparisons.

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 non-serious adverse event terms

The registry reports no serious adverse events in either arm among those listed as at risk, and no deaths. It records one other adverse event in the ePrEP arm and none in standard care. No serious adverse-event terms are listed. The “other” event is not identified by type in the registry record, so its nature and clinical context cannot be described.

The adverse-event risk sets are recorded as 108 for ePrEP and 109 for standard care. These numbers differ from the outcome denominators for the biomarker comparisons, and the record does not explain the distinction. The safety counts should therefore be read according to their own recorded risk sets rather than combined with the efficacy-related biomarker results.

Zero recorded serious events does not establish that an intervention has no safety risks. It describes the events reported in this trial record; interpretation is limited by the available event detail, observation period, and absence of a fuller safety analysis. The registry does not report additional information about event severity, timing, relatedness, or how adverse events were collected.

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

The primary finding is a difference in the recorded proportion meeting the biomarker-based adherence threshold at 6-month follow-up, with the posted data favoring a higher observed proportion in the ePrEP arm. The estimate and its confidence interval describe the size and uncertainty of that specific comparison. They do not establish that every participant assigned to ePrEP had better adherence, or that the same result would occur in other populations or care settings.

The endpoint is not a direct measure of all aspects of PrEP care. It reflects TFV-DP in a self-collected specimen and a registry-defined threshold tied to medication-taking over approximately the month before collection. It does not by itself measure access, satisfaction, persistence throughout the full follow-up, or other health outcomes. Nor does the biomarker comparison answer whether the telemedicine system is more acceptable, feasible, or cost-effective; those outcomes are not reported in the registry record described by the registry record.

The 12-month comparison does not show a clear difference in the posted data, but that is not evidence that the arms are equivalent. Its uncertainty includes differences in either direction. The registry does not report an analysis that directly compares change between the primary and secondary time points, so the two estimates should not be interpreted as a formal test of persistence or waning.

The study’s randomized parallel design supports the aim of comparing ePrEP with standard care, but important implementation and analysis details are not reported. In particular, the record does not explain the outcome denominators, missing-data procedures, or analysis populations. Those limitations constrain how confidently the observed comparisons can be generalized to everyone enrolled.

These results are statistical evidence about the posted biomarker outcome, not medical advice or a conclusion about an individual’s care. They should be interpreted within the study population, the measured endpoint, the reported follow-up times, and the uncertainty and omissions in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why a registry outcome’s label and its actual measurement need to be read together. The primary title refers to TFV-DP levels, while the posted comparison is a count of participants meeting a threshold. That distinction changes the estimand: the reported contrast concerns classification at a cutpoint, not a difference in average biomarker concentration.

It also shows how follow-up timing and outcome availability shape interpretation. The 6-month primary comparison and 12-month secondary comparison use different denominators, and the registry does not explain why. A statistically clear primary contrast does not automatically describe the later time point, while a later non-significant comparison does not prove equivalence or a change in effect. Each result must be interpreted at its own follow-up and with its own uncertainty.

The sample-size illustrations provide another statistical lesson. Planning numbers based on an observed effect are not the same as the study’s original design rationale, and a smaller planning target effect requires a larger sample under the stated assumptions. Such calculations can inform future study design, but do not establish what the completed trial was powered to detect.

Finally, the record highlights the importance of transparent reporting beyond a p-value. Analysis populations, missing-data methods, multiplicity handling, and randomization procedures are relevant to judging a randomized comparison. Their absence does not erase the posted results, but it limits the conclusions that can be drawn from them and makes careful separation of observed evidence from unreported design choices essential.

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.

A central limitation is that the registry does not explain why the outcome denominators are smaller than enrollment or why the 12-month denominators differ from those at 6 months. Without details about specimen availability and participant flow, it is difficult to judge how representative the observed biomarker results are of the randomized groups. Missingness could affect the interpretation if availability of a specimen is related to adherence or care engagement, but whether that occurred is not reported.

The primary endpoint reduces biomarker measurements to a binary cutpoint. This makes the outcome easier to interpret as meeting a stated adherence threshold, but removes information about variation in levels within each classification. The registry also gives medication-specific cutpoints and mentions decision rules for certain medication-reporting situations, while the full rules are not available. This limits independent assessment of how every participant was classified.

Important trial and analysis details are absent from the registry record, including the randomization method, allocation concealment, baseline characteristics, analysis population, missing-data approach, and exact inferential procedures. Multiplicity handling is not reported. The posted p-values are unadjusted, and no adjusted analysis is listed. These gaps limit assessment of robustness and the role of possible imbalances or analytic choices.

The intervention and comparator descriptions are incomplete. The record names some components of ePrEP and the standard-care referral approach, but does not provide enough detail to assess intervention fidelity, participant use, or differences in access after referral. Safety reporting is also limited: one other event is recorded without a term, and no further event context is available. These points restrict interpretation of implementation and safety beyond the recorded counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Electronic Pre-exposure Prophylaxis (PrEP) Initiation and Maintenance Home Care System — NCT03729570.
• Registry record last updated 2024-10-18; status last verified 2024-10.
• Results first posted 2024-06-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes NCT03729570, a completed, randomized, parallel-group, unmasked study of an electronic home-care system intended to support PrEP initiation and continued care among adolescent men who have sex with men in rural and small-town areas. Enrollment was 217. The listed study start date is 2019-05-28 and primary completion date is 2022-05-31.

The primary outcome is a threshold-based TFV-DP biomarker measure at 6-month follow-up. The posted counts are 17 of 31 in ePrEP and 7 of 26 in standard care, with an unadjusted risk difference of 0.279 and p = 0.033. The 12-month secondary comparison is less distinct and has p = 0.917. The registry also records no serious adverse events or deaths and one other adverse event in ePrEP.

The registry does not report key details on allocation procedures, missing-data handling, analysis populations, multiplicity, or the original sample-size rationale. Those omissions limit interpretation beyond the observed comparisons and their stated uncertainty.