PrEP iT! Mobile App Intervention: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PrEP iT! Mobile App Intervention (NCT04509076), a randomized na study. The primary outcome is High Protective Level of PrEP Adherence From Tenofovir Diphosphate (TVF-DP) Levels.

2. Clinical Question

3. Trial Design

PrEP iT! was a randomized, parallel-group pilot trial with no masking. The registry lists an enrollment of 80 and marks the study as completed. The recorded study start was 2021-03-01, and the primary completion date was 2022-04-15. The trial was sponsored by San Diego State University. Its phase is listed as NA.

One arm received PrEP iT! In addition to usual PrEP care; the other received usual PrEP care only. The intervention was a mobile-optimized website tailored to young men who have sex with men who were taking PrEP. Usual care was described as clinic visits every 3 months in the initial period after PrEP initiation, with HIV and STI screening and laboratory toxicity testing. The registry does not report further detail about the duration or content of website use, the randomization procedure, or the specific usual-care arrangements experienced by individual participants.

The study summary describes two aims: developing and refining the mobile intervention through focus groups and input from a community advisory board, and conducting a pilot randomized trial to assess feasibility, acceptability and preliminary impact. The primary endpoint posted for the trial is a count of participants classified as having a high protective level of PrEP adherence at the 6-month follow-up assessment. The endpoint counts are 13 of 27 in the PrEP iT! plus usual-care arm and 15 of 24 in the usual-care-only arm. These are the endpoint denominators; the registry does not explain how they relate to the enrollment figure or whether participants without posted endpoint data were missing, ineligible for this outcome, or excluded for another reason.

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:

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 High Protective Level of PrEP Adherence From Tenofovir Diphosphate (TVF-DP) Levels, measured over 6-month follow up assessment.

The primary endpoint is the count of participants classified as having a high protective level of PrEP adherence at the 6-month follow-up assessment. Classification was based on tenofovir diphosphate (TVF-DP) levels measured in dried blood spot specimens. The registry description identifies thresholds of 800 or greater for FTC-TDF and 950 or greater for FTC-TAF. The posted results concern participants meeting the high protective-level classification.

This is a binary outcome at the participant level: each participant is classified as either meeting the stated threshold or not. Counting participants in each group makes the outcome suitable for a comparison of the proportions classified as high protective level. Biomarker-based classification provides a measurement tied to drug levels in a specimen, rather than relying only on a participant’s report of medication-taking. That general distinction explains why such a measure can be useful when studying adherence; it does not establish that the measure captures every aspect of adherence or care retention.

The endpoint is an adherence classification, not a direct count of HIV infections, retention in care, or a measure of intervention acceptability. The registry record does not report the laboratory procedures beyond the dried blood spot specimen and threshold description, or how values at or below the thresholds were handled beyond classifying participants as not having a high protective level.

7. Results Posted in the Registry

• Usual PrEP Care Only: 62.5% (15/24) versus 48.1% (13/27) on control; risk difference 14.4 percentage points (95% CI -12.7 to 41.4), risk ratio 1.30 (0.79–2.14); unadjusted two-proportion z-test p = 0.304.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either met the high protective-level classification or did not. For a binary endpoint, a group’s event proportion is the number of participants meeting the criterion divided by the number assessed in that group. The posted counts are 13 of 27 for PrEP iT! plus usual care and 15 of 24 for usual care only. The count is not a continuous measure of drug level; the registry presents the threshold-based classification.

What does the risk difference describe?

In general, a risk difference expresses the difference between two group proportions on the original probability scale. A value of zero represents equal proportions. Positive or negative values indicate the direction of the subtraction, so the comparison’s stated orientation matters. In this record, the risk difference compares usual care with PrEP iT! plus usual care. The posted estimate is positive, corresponding to the higher observed proportion in the usual-care-only arm. Its confidence interval includes zero, so the estimate is not precise enough to rule out no difference or a difference in the other direction.

How do relative measures differ?

In general, a risk ratio compares one group’s probability with the other group’s probability. A value of one represents equal probabilities. An odds ratio compares odds rather than probabilities, and a value of one represents equal odds. The registry posts both measures, with confidence intervals that span their respective no-association values. Relative measures can express a contrast differently from an absolute risk difference, but neither removes uncertainty in the underlying counts. When the endpoint is common, odds ratios can also appear farther from the no-association value than risk ratios; that is a general property of the measures, not a separate conclusion about this intervention.

What does the p-value contribute?

In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it is not a measure of the size or importance of an effect. The posted unadjusted p-value is 0.304. Read alongside the point estimate and confidence interval, it indicates that this comparison does not provide strong evidence against the null hypothesis under the unadjusted test. It does not prove that the groups are identical.

Confidence intervals and p-values address related but distinct questions. A confidence interval conveys a range of estimates compatible with the data under the method used, while the p-value summarizes evidence against a particular null value. Here, the risk-difference interval crosses zero, which corresponds to the no-difference value. The width of the interval also conveys that the estimate is uncertain. General interpretation should account for the magnitude and precision of an estimate, not only whether a p-value crosses a chosen threshold.

What can be inferred from randomization?

In general, random allocation is intended to make treatment groups comparable, on average, with respect to factors measured and unmeasured at baseline. It does not guarantee balance in every trial, especially when the groups contributing endpoint data are limited. The registry identifies the allocation as randomized, but it does not report the sequence-generation method, concealment procedures, or baseline characteristics. The record therefore supports describing the study as randomized, but not a detailed assessment of how randomization was implemented or whether groups were balanced.

The record identifies a parallel model and no masking. A parallel design assigns participants to one of the study arms and follows the assigned groups. General methodological reasoning recognizes that lack of masking can influence behavior, care, or assessment in some settings, but the record does not report whether such influences occurred in this trial. It also does not describe endpoint assessor masking or the laboratory workflow.

What does the pilot context imply?

A pilot trial can inform whether a larger study is practicable and can produce preliminary estimates, but an estimate from a pilot can be unstable. The study summary explicitly frames the randomized trial as a pilot to assess feasibility, acceptability and preliminary impact. The registry does not report a statistical analysis plan, original sample-size justification, interim analyses, or a prespecified approach to hypothesis testing. Those details cannot be inferred from the posted counts or from a planning illustration based on the observed effect.

The registry lists two outcome measures and no posted secondary results. It records zero analysis entries. This makes it important to distinguish the endpoint result from an account of the full analytic process: the record does not explain whether other analyses were conducted, how outcomes were selected for reporting, or whether any adjustments were made. The posted comparison should be read as the available registry result, not as evidence that unreported analyses were or were not performed.

10. Confidence Intervals and Precision

The risk-difference confidence interval extends from a negative value to a positive value. Because zero lies within that interval, the posted data do not rule out no difference between the groups. The interval also permits effects in either direction, so the point estimate should not be interpreted as a precise estimate of the difference that would be expected in a broader population.

In general, a confidence interval is a range produced by a statistical procedure that reflects uncertainty in an estimate. It is not a guarantee that the true value lies within the particular interval, nor does it describe the range of individual participants’ outcomes. Its width is relevant: a wider interval means a less precise estimate. The comparison’s interval is broad enough to include materially different possibilities, including no difference. The registry does not report a prespecified threshold for what difference would be clinically or programmatically important, so the interval cannot be judged against such a threshold from this record.

The posted risk-ratio and odds-ratio intervals also include their respective null values. Their breadth reinforces that the relative comparisons are uncertain. These measures use different scales, and their numerical values should not be compared directly with the risk difference as if they were the same quantity.

The endpoint counts are based on 27 participants in the intervention arm and 24 in the usual-care arm. The registry’s overall enrollment is 80, and it does not explain the relationship between enrollment and these endpoint denominators. Without information about missing observations, exclusions, or the analysis population, precision cannot be assessed independently of those reporting gaps. The interval describes uncertainty for the posted comparison under its calculation; it does not address possible bias from missing data or other design and reporting limitations.

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 figures are planning illustrations expressed as participants per arm, not total events. They use the observed effect as a starting point and show planning for 100%, 75% and 50% of that observed effect. For the observed effect, the illustration gives 188 participants per arm for 80% power and 251 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 336 participants per arm for 80% power and 450 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 761 participants per arm for 80% power and 1,017 participants per arm for 90% power.

The stated 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. In plain terms, the 80% power column gives the number of participants per arm under which the planning model would have an 80% chance of detecting the specified effect at the stated significance level, if the assumptions hold. The 90% column uses a higher chance of detection under the same planning framework.

Smaller effects are harder to distinguish from random variation, so the illustration requires more participants per arm when the target effect is a smaller fraction of the observed effect. These values are planning calculations, not the trial’s original design assumptions; the original sample-size justification is not reported in the registry record. They are not observed power.

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 = 0.481; treatment proportion p₁ = 0.625; average p̄ = 0.553.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7031 = 1.3780.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6957 = 0.5855.
4. n = (1.3780 + 0.5855)² / (0.1435)² = 187.2, rounded up to 188 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 <- 0.481481481481481                          # control proportion
p1 <- 0.625                          # 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(4509076)
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 = 188 (80% power), 251 (90% power)
 75% of observed effect: n per arm = 336 (80% power), 450 (90% power)
 50% of observed effect: n per arm = 761 (80% power), 1,017 (90% power)
power.prop.test: 187.2 
Simulated power at n = 188 per arm: 0.812 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists two outcome measures, identifies a primary endpoint, and posts no secondary outcome results. It also records zero analysis entries. The registry record does not report a multiplicity adjustment, a hierarchy of hypotheses, or an analysis plan specifying how multiple outcomes or comparisons were to be handled. It is therefore not possible to determine from the record whether the posted p-value was selected from a larger set of analyses or whether any adjustment was planned.

In general, multiplicity arises when several hypotheses are tested or several outcomes are examined. Repeated testing can increase the chance of at least one apparently unusual result under a collection of null hypotheses. Prespecified priorities and appropriate methods can help address this concern. This general point does not establish that multiplicity affected the posted result; the relevant analytic details are not reported in the registry record.

The record does not report how missing endpoint measurements were handled, whether participants were excluded from the primary comparison, or whether any imputation was used. It also does not identify the analysis population, such as whether the comparison followed original randomized assignment regardless of intervention use. Since enrollment is listed as 80 and the endpoint denominators are 27 and 24, the relationship between those numbers and any missing or excluded participants is not reported.

These omissions limit assessment of whether the comparison preserves the advantages of randomization and how sensitive the result might be to unavailable endpoint data. In general, complete-case comparisons can be biased when the probability of having an observed outcome differs by group or relates to the outcome. That is a methodological possibility, not a claim that it occurred in this trial. The registry also does not report whether analyses were adjusted for baseline variables or whether other sensitivity analyses were conducted.

14. 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.

The registry reports zero serious adverse events among 40 participants at risk in the PrEP iT! plus usual-care group and zero among 40 at risk in the usual-care-only group. It also reports zero other adverse events in the same at-risk groups and zero deaths in each group. No serious adverse event terms are listed.

These figures describe the adverse-event entries in the registry. Zero reported events does not establish that no events occurred outside the scope or duration of the recorded assessment, and it does not demonstrate that the groups have identical safety profiles. In general, the ability to detect uncommon events depends on how many participants are assessed and how long they are followed. The registry record does not report the adverse-event collection period, definitions, or detailed ascertainment procedures.

The adverse-event denominators are 40 in each group, whereas the primary endpoint denominators are 27 and 24. The record does not explain this difference. The safety counts should therefore be read with their own at-risk denominators and not treated as if they came from the same analysis population as the primary endpoint.

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

The result describes how many participants in each arm met the registry’s high protective-level adherence classification at the 6-month follow-up assessment. The count was 13 of 27 in the PrEP iT! plus usual-care arm and 15 of 24 in the usual-care-only arm. The posted comparison estimates a difference between the groups, but its confidence interval crosses the value representing no difference, and the unadjusted p-value is 0.304. These data leave substantial uncertainty about the direction and size of any underlying difference.

The findings do not establish that PrEP iT! improves or reduces adherence, and they do not establish equivalence between the arms. A result that is not statistically compelling is not proof that a difference is absent. Conversely, a point estimate in one direction does not show that the intervention caused a difference. The limitations of the posted comparison and the pilot setting should be considered alongside the estimate.

The primary outcome is a biomarker-based adherence category, not a direct measure of HIV incidence, retention in care, or intervention acceptability. The study summary names feasibility and acceptability as aims, but the registry record does not post secondary results addressing those aims. It also does not provide enough detail about missing endpoint data or the analysis population to determine how the posted counts relate to all enrolled participants.

In general, pilot results are useful as preliminary evidence and can help motivate further study, but estimates from a pilot may be imprecise. The planning illustrations based on fractions of the observed effect show how strongly projected participant requirements depend on the effect chosen for planning. They do not validate the observed estimate or establish what a later trial would find.

The interpretation should remain limited to the registry’s reported endpoint and comparison. It does not support a recommendation about PrEP care or a conclusion about the clinical impact of the mobile website. Those questions require evidence beyond these posted pilot counts.

16. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the gap between a promising research question and a precise comparative estimate. The study tested a mobile-optimized peer-support intervention in a randomized parallel-group pilot, while its primary outcome was a threshold-based adherence classification at the 6-month follow-up assessment. That design produces an interpretable group comparison, but the endpoint counts are limited and the confidence interval remains broad.

The comparison includes uncertainty in both directions. The point estimate follows the observed pattern of counts, with more participants meeting the endpoint in the usual-care-only arm, but the confidence interval does not exclude no difference. This is a useful reminder that the direction of a point estimate and the strength of evidence are different aspects of a result. Counts alone cannot resolve the uncertainty, and a p-value should not substitute for examination of the estimate and interval.

The pilot context also matters. The study summary names feasibility, acceptability and preliminary impact as aims, while the posted primary result concerns adherence. The available record does not include secondary results that would address the full range of aims. It also does not explain the difference between enrollment and the primary endpoint denominators, or describe missing-data handling and the analysis population. These reporting gaps affect how confidently readers can connect the observed endpoint counts to the randomized trial as a whole.

Finally, planning illustrations based on the observed effect emphasize the sensitivity of sample-size projections to the effect chosen. More conservative targets based on smaller fractions of the observed effect require larger per-arm samples under the stated assumptions. The trial’s original sample-size justification is not reported, so those illustrations should be treated as prospective planning examples rather than as a description of the original design.

17. 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 registry record does not report the randomization sequence method, allocation concealment, participant flow, or baseline characteristics. It identifies the study as randomized and unmasked, but does not explain how those procedures were implemented. As a result, readers cannot assess baseline comparability or determine whether the groups contributing endpoint data remained comparable after any missing observations or exclusions.

The study summary identifies young men who have sex with men aged 18-29 as the intended target, but the registry does not report detailed characteristics of the participants contributing to the endpoint. It also does not report the extent of intervention engagement, website use, or adherence to assigned care. Such details would help characterize what exposure the comparison represents, but they cannot be inferred from assignment alone.

The outcome denominators, 27 and 24, are smaller than the registry enrollment of 80. The record does not give a participant flow explanation or state whether the difference reflects missing specimens, exclusions, timing, or another cause. The adverse-event denominators are 40 in each arm, and their relationship to the endpoint populations is also not explained. Follow-up and adverse-event ascertainment details are not reported.

The record lists two outcome measures but no secondary results, and it records zero analysis entries. It does not report the statistical analysis plan, original sample-size justification, missing-data methods, analysis population, interim analyses, or adjustment for multiple comparisons. These are limits on what can be assessed from the registry record; they do not show that any particular procedure was or was not used.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: PrEP iT! Mobile App Intervention — NCT04509076.
• Registry record last updated 2023-07-07; status last verified 2023-06.
• Results first posted 2023-06-15.
• 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.

21. Record Summary

NCT04509076, titled PrEP iT! Mobile App Intervention, is a completed randomized, unmasked, parallel-group pilot sponsored by San Diego State University. The registry lists enrollment of 80, a start date of 2021-03-01, and primary completion on 2022-04-15. The intended population described in the study summary is young men who have sex with men, aged 18-29.

The comparison was PrEP iT! plus usual PrEP care versus usual PrEP care only. The primary endpoint was a high protective-level PrEP adherence classification based on TVF-DP levels in dried blood spot specimens at the 6-month follow-up assessment. The posted counts are 13 of 27 and 15 of 24, respectively. The risk-difference interval includes zero, and the unadjusted p-value is 0.304.

The trial summary describes aims concerning intervention development, feasibility, acceptability and preliminary impact. The registry record does not report secondary results, the analysis population, missing-data handling, or the original sample-size justification.