Pre-Exposure Prophylaxis (PrEP) Adherence Monitoring Using Dried Blood Spots: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pre-Exposure Prophylaxis (PrEP) Adherence Monitoring Using Dried Blood Spots (NCT02022657), a randomized phase 1, phase 2 study. The primary outcome is Steady State Concentrations of TFV-DP for Different Dosing Patterns of Truvada.

2. Clinical Question

The study is described as a randomized crossover, so participants were assigned to sequences containing two dosing regimens rather than only one parallel-group assignment. The central measurement question is whether the biomarker concentration differs across prescribed dosing levels under directly observed dosing. That setup can help characterize how a measured biomarker varies with known dosing exposure, but the posted outcome is a set of regimen-specific means and standard deviations. The registry record does not report an adherence prediction model’s performance or a direct measure of prediction accuracy.

3. Trial Design

The registry describes a randomized, unmasked, crossover study with phase labels of PHASE1 and PHASE2. It lists 52 participants enrolled and a completed study. The start is recorded as 2014-04 and primary completion as 2016-11. The brief summary describes healthy HIV-uninfected adults at low risk for HIV infection and says that participants were randomized to one of six sequences involving two directly observed dosing regimens. The sequence options combine 33%, 67%, and 100% of daily dosing in different orders.

Each regimen was planned to last approximately 12 weeks, with an approximately 12 week washout period between regimens. Dried blood spots were to be collected at regular intervals, including during washout. The primary outcome timeframe says concentrations were assessed every 2 weeks during dosing periods and at steady state, week 12 for the first dosing period and week 36 for the second dosing period. These statements describe the planned collection and assessment schedule; the registry record does not report the realized visit schedule or any deviations.

The primary-outcome population description states that 48 participants were included and that each participant was randomized to two of the three regimens, for a total of 32 participants per regimen. It also notes that 2 participants completed only the first regimen. The posted outcome counts are 30 for the 33% regimen, 32 for the 67% regimen, and 32 for the 100% regimen. The registry record does not explain in detail how the outcome counts relate to the enrollment total of 52 or provide a participant flow account.

Because the design is crossover, observations from different regimens may come from the same participant. The regimen counts should therefore not automatically be read as counts of unrelated participants across independent groups. The registry record does not report how the crossover structure, treatment sequence, within-participant correlation, period effects, or potential carryover were handled in the analysis. It also does not report the trial’s original sample-size justification or full statistical analysis plan.

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: 52 subjects from 2 sites were analyzed-- CU enrolled only 34.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The total number of participants was 48. Each participant was randomized to 2 of 3 dosing regimens for a total of 32 participants each, however 2 participants completed only the first regimen.

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: Arms were combined to be consistent with protocol subject randomization. Subjects were randomized to one of six arms. "Holiday" and "intermittent" groups for 33 and 67% dosing were combined because drug concentrations didn't differ between groups (PMID: 29038282). Combined arms best categorize the study and population.

6. Primary Endpoint

The registry lists the primary outcome as Steady State Concentrations of TFV-DP for Different Dosing Patterns of Truvada, measured over Assessed every 2 weeks during the dosing periods and at steady-state, week 12 for the first dosing period and week 36 for the second dosing period..

The primary endpoint is the mean concentration of tenofovir-diphosphate, or TFV-DP, measured in dried blood spots. The unit is fmol/punch. The outcome title specifies steady-state concentrations for different Truvada dosing patterns, and the description identifies the 33%, 67%, and 100% daily dosing regimens. The outcome is reported as a mean with standard deviation for each regimen.

TFV-DP in dried blood spots was selected as a biomarker to characterize drug exposure associated with different known dosing levels. The study objective was to define the mean, variance, and dose proportionality across dosing regimens and use that information to establish a model for predicting adherence from DBS measurements. This is the stated rationale for measuring the concentration: it can be examined in relation to prescribed dosing exposure, with the longer-term objective of estimating adherence over the preceding 1-3 months.

The outcome directly reports biomarker concentration rather than adherence itself, clinical outcomes, or the accuracy of a prediction model. The posted means and standard deviations describe the concentration distributions by regimen. The registry record does not report model calibration, prediction error, sensitivity, specificity, or another measure of predictive performance. Therefore, the endpoint supports describing concentration patterns across the dosing regimens, but the posted endpoint alone cannot demonstrate how well DBS concentrations classify or predict adherence in other settings.

7. Results Posted in the Registry

• DOT-DBS Dosing 67%: mean 997.00 versus 530.00 on control; difference 467.00 (95% CI 358.39 to 575.61), standardized effect d = 2.11; z-test p = <0.001.
• DOT-DBS Dosing 100%: mean 1,605 versus 530.00 on control; difference 1,075 (95% CI 923.58 to 1,226), standardized effect d = 3.45; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: each measurement is a concentration in fmol/punch, and the registry reports a mean and standard deviation for each dosing regimen. A mean describes the center of the observed concentration values, while the standard deviation describes the spread of individual values around that mean. Neither statistic gives the full shape of the concentration distribution. The registry record does not report additional distributional summaries or plots of individual participant values.

What does a mean difference describe?

A mean difference expresses the distance between two group means in the outcome’s original units. The recalculated comparison between 67% and 33% is 467.0 fmol/punch, and the comparison between 100% and 33% is 1075.0 fmol/punch. The direction is defined by the higher-dose regimen relative to the 33% regimen, so positive estimates correspond to higher mean concentrations in the higher-dose regimen. These are unadjusted differences calculated from the posted summary statistics.

The mean difference is easy to interpret in the measurement scale, but it does not describe every participant’s response. It also should not be interpreted as a within-person change unless the analysis explicitly uses paired participant data. Although the trial is described as a crossover, the recalculated comparisons do not incorporate pairing or other design features. The registry record does not report estimates from a crossover-specific model.

How should the standard deviation be read?

The regimen standard deviations are 159.0, 267.0, and 405.0 fmol/punch for 33%, 67%, and 100% dosing, respectively. Standard deviation describes variability among observed concentrations within a regimen; it is not the uncertainty of the mean. The standard error instead describes the estimated uncertainty of a mean and depends on the observed spread and number of observations contributing to it. The comparison calculations use the posted regimen summaries, but the registry record does not provide details of a model used to estimate these quantities in a crossover framework.

Over-dispersion is a general statistical concern when the observed spread is larger than assumed by a model. If over-dispersion is present and not addressed, standard errors may be too small and confidence intervals may be too narrow. This is a general explanation, not a claim that over-dispersion was found in this trial. The registry record does not report a distributional or over-dispersion assessment.

What does the confidence interval contribute?

A confidence interval gives a range of values compatible with the estimate under the calculation’s statistical assumptions. For the 67% versus 33% comparison, the 95% interval is 358.4 to 575.6 fmol/punch. For the 100% versus 33% comparison, it is 923.6 to 1226.0 fmol/punch. The intervals convey estimation uncertainty more directly than a p-value alone: they show both the direction and a range of plausible mean differences under the unadjusted calculation.

Confidence intervals do not guarantee that the true effect lies in the particular interval, and they do not account for limitations omitted from the calculation. Here, the calculations do not incorporate the crossover correlation or report adjustment for sequence, period, or carryover. They also do not resolve potential bias from incomplete outcome data. Thus, interval width should be interpreted alongside the design and missing-data information, not as a complete measure of uncertainty in every possible analysis.

What does the p-value say?

The unadjusted p-value is <0.001 for each posted regimen comparison. In general, a p-value describes how incompatible the observed data are with a specified null model, assuming the model and its assumptions hold. A small p-value is not the probability that the null hypothesis is true, nor does it establish clinical importance or model-prediction accuracy. Since the registry does not report a detailed analysis plan and the comparisons are unadjusted recalculations, these p-values should not be mistaken for results from a documented primary crossover analysis.

The record lists one primary outcome measure and no posted analyses. It does not report the exact statistical test, the treatment of repeated measurements, whether the primary endpoint was prespecified at the steady-state visits, or any multiplicity adjustment. The statistical method underlying sponsor-reported results is not reported in the registry record. That absence makes it important to distinguish the posted summary statistics and recalculations from a complete account of the planned and conducted analysis.

Why does the crossover design matter?

In a crossover study, a participant may contribute observations under more than one regimen. Such observations are usually correlated because they come from the same person. A paired or mixed-effects analysis can account for that correlation; a simple comparison that treats groups as independent does not. The registry record identifies a crossover design and a washout period, but does not report whether the statistical analysis incorporated paired measurements, sequence allocation, period, or carryover. No assumption about that analysis can be made from the posted record.

The outcome population description says participants were assigned to two of three regimens and notes that 2 completed only the first regimen. This incomplete crossover participation makes the analysis population and handling of missing second-period measurements important. The registry record does not report an intention-to-treat or per-protocol definition, a method for missing observations, or sensitivity analyses. Consequently, the unadjusted comparisons are useful descriptive summaries but do not answer every design-based inferential question.

10. Confidence Intervals and Precision

The recalculated 95% confidence interval for the mean difference between 67% and 33% dosing is 358.4 to 575.6 fmol/punch. For the comparison between 100% and 33% dosing, it is 923.6 to 1226.0 fmol/punch. Both intervals lie above zero, and their widths express the uncertainty in the corresponding unadjusted estimates under the calculation assumptions. The estimates are relatively precise in the narrow sense that the intervals occupy limited ranges around their point estimates, but this does not account for omitted design features or missing-data concerns.

The confidence intervals apply to differences between regimen means, not to the range of concentrations expected among individual participants. The standard deviations describe participant-level spread within each regimen, while the intervals describe uncertainty about a mean difference. These answer different questions and should not be substituted for one another. The registry record does not report confidence intervals for the individual regimen means.

Precision is also conditional on the analysis method. The displayed recalculations are unadjusted and do not account for the crossover structure. If within-participant correlation, regimen sequence, period, or carryover affects the outcome, an analysis that incorporates those features could yield different standard errors and intervals. The registry record does not report such estimates or enough detail to judge their impact. Nor does it report how missing measurements were handled. Accordingly, the intervals quantify precision under the simple recalculation, not every source of uncertainty in the study.

The p-values of <0.001 for both comparisons indicate strong incompatibility with a zero mean difference under the unadjusted calculation’s assumptions. They do not establish that the differences are important for predicting adherence, and they cannot establish the performance of the proposed model. Precision of the mean contrast and validity of a prediction tool are separate questions.

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 planning figures are participants per arm for 80% power and participants per arm for 90% power. They are based on two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The planned effect to detect is the stated fraction of the observed effect. These are planning illustrations, not observed power.

For the 67% versus 33% comparison, planning for 100% of the observed effect gives 4 participants per arm for 80% power and 5 for 90% power. Planning for 75% of the observed effect gives 7 per arm for 80% power and 9 for 90% power. Planning for 50% of the observed effect gives 15 per arm for 80% power and 19 for 90% power.

For the 100% versus 33% comparison, planning for 100% of the observed effect gives 2 participants per arm for 80% power and 2 for 90% power. Planning for 75% of the observed effect gives 3 per arm for 80% power and 4 for 90% power. Planning for 50% of the observed effect gives 6 per arm for 80% power and 8 for 90% power. The 80% and 90% columns describe the chance of detecting the specified effect under the planning assumptions if that effect is true; a higher target power generally requires more participants. Smaller effects need more participants to detect than larger effects.

These figures use effects estimated from the observed comparisons and are not the trial’s original design calculations. The registry record does not report the original sample-size assumptions or justification. The stated assumptions use equal allocation and a two-arm normal approximation; they do not describe the crossover structure or account for its within-participant design. The illustrations should therefore not be read as a reconstruction of the trial’s planned enrollment.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 467.000; pooled standard deviation σ = 221.476.
2. n = 2 × (1.96 + 0.842)² × 221.476² / 467.000² = 3.5, rounded up to 4 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 <- 467                      # observed difference in means
sigma <- 221.476409578989                     # 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(2022657)
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 = 4 (80% power), 5 (90% power)
 75% of observed effect: n per arm = 7 (80% power), 9 (90% power)
 50% of observed effect: n per arm = 15 (80% power), 19 (90% power)
power.t.test: 4.7 
Simulated power at n = 4 per arm: 0.696 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and no posted secondary outcome measures. It also lists no posted analyses. It does not report a statistical analysis plan, a testing hierarchy, or a multiplicity adjustment. Two unadjusted comparisons are available: 67% versus 33%, and 100% versus 33%. Their p-values should be interpreted as unadjusted rather than as values adjusted for multiple comparisons. The registry record does not explain whether these comparisons were prespecified or how any other analyses were handled.

The primary-outcome description states that the total outcome population was 48 and that 2 participants completed only the first regimen. The posted outcome counts are 30 for 33% dosing and 32 for each of the 67% and 100% regimens. These counts indicate that the number of observations contributing to the reported regimen summaries is not identical across all regimens. The registry record does not report reasons for incomplete participation, participant disposition by sequence, or whether the missing measurements were related to outcomes or regimen assignment.

The record does not specify an intention-to-treat population, a per-protocol population, or another formal analysis-population definition. It does not say whether missing observations were excluded, imputed, or addressed through a model, and no sensitivity analyses are reported. Since the design is crossover, incomplete regimen data could affect paired comparisons and the representation of treatment sequences. The available summaries do not reveal how these issues were addressed.

There is also no reported detail about the statistical treatment of repeated measurements taken every 2 weeks, the steady-state visit selection, or the relation between observations within a participant. The registry record does not report adjustments for sequence, period, or carryover. These omissions do not establish that such methods were not used; their use is not reported in the registry record. They do limit independent assessment of how closely the posted comparisons reflect the randomized crossover design.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anxiety (2.1%), pneumonia (2.1%).

The registry lists safety information for all dosing regimens combined, with 48 participants at risk for serious adverse events and 1 participant affected. The top serious adverse event terms are Anxiety and Pneumonia, each reported as 2.1%. The record lists 48 participants at risk for other adverse events and 48 affected. Deaths are listed as 0.

These figures describe the safety reporting in the registry record, not a comparison of adverse event rates between the 33%, 67%, and 100% regimens. The adverse-event group combines all dosing regimens, and the record does not provide regimen-specific serious-event counts or a detailed event-level account. The two listed terms are reported as the top serious event terms; the record does not provide further detail about timing, severity beyond the serious-event classification, or attribution.

The count of participants affected should not be interpreted as the number of event episodes; the registry record does not clarify whether a participant could have more than one event. The safety data do not establish causation. They are descriptive registry counts and do not, by themselves, support comparative safety conclusions between dosing regimens.

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

The posted results show increasing mean TFV-DP concentrations across the 33%, 67%, and 100% directly observed dosing regimens: 530.0, 997.0, and 1605.0 fmol/punch, respectively. The recalculated unadjusted comparisons show higher means for 67% and 100% dosing than for 33% dosing, with p < 0.001 for each comparison. The confidence intervals describe the range of mean differences compatible with those calculations.

This result is relevant to the stated objective of investigating TFV-DP concentrations in dried blood spots under known dosing exposure. It describes an association between regimen level and mean biomarker concentration in this study’s outcome summaries. It does not show that a DBS measurement can accurately determine a particular participant’s adherence, nor does it validate the proposed model for estimating adherence over the preceding 1-3 months. The registry record does not report model performance or external validation.

The findings also do not establish dose proportionality solely from the three means. Dose proportionality concerns the form of the relationship between dose and concentration; the registry record provides the stated objective but not a reported formal test or model result establishing that relationship. Similarly, group means do not reveal the extent of overlap in individual measurements or the accuracy of classifying individual dosing behavior.

The crossover design and directly observed regimens provide the study’s setting, but the posted comparisons are unadjusted recalculations and do not account for participant-level pairing. Details of analysis population, missing data, sequence, period, and carryover are not reported. These limitations qualify how confidently the group comparisons can be generalized beyond the summaries. The data are not a basis for medical advice or conclusions about clinical benefit; they are biomarker measurements under the described study regimens.

16. Why This Trial Matters Statistically

This trial raises a statistical question that is important for biomarker research: whether a biological measurement changes in a predictable way across known levels of drug exposure. The primary endpoint uses TFV-DP concentrations in dried blood spots, while the stated longer-term aim is to use those concentrations to predict adherence over the preceding 1-3 months. Separating these questions is essential. A concentration gradient across regimens can support characterization of exposure, but prediction requires evaluating how well measurements estimate adherence for individuals.

The three posted means form an ordered pattern across the dosing levels, and the recalculated comparisons quantify two contrasts against the 33% regimen. This provides a concise description of group-level differences in the biomarker. At the same time, the study’s crossover structure illustrates why analysis design matters: the same participant may contribute results under multiple regimens, creating correlated observations. Treating those observations as independent can fail to reflect the randomized design, so the analysis method should make clear how participant-level dependence is handled.

The record also illustrates the distinction between statistical significance and useful prediction. The reported unadjusted p-values are <0.001, but a small p-value does not show how accurately DBS concentrations classify adherence, nor whether the prediction is precise enough for a particular purpose. Prediction requires its own evaluation, and that performance is not reported in the registry record.

Finally, the difference between registry enrollment and the primary-outcome population, and the note that 2 participants completed only the first regimen, highlight the importance of clear participant accounting. Transparent reporting of analysis populations, missing outcomes, and crossover methods is needed to judge the precision and scope of a result. The registry record gives useful concentration summaries, but does not provide all of those analytic details.

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 primary limitation for interpretation is that the posted comparisons are unadjusted recalculations from regimen-level summary statistics. The study is described as randomized and crossover, but the registry record does not report a crossover-specific analysis incorporating within-participant correlation. It also does not report adjustment for sequence, period, or potential carryover. The approximately 12 week washout period is described in the study summary, but whether it was sufficient or how carryover was assessed is not reported.

The registry lists enrollment of 52, whereas the primary-outcome description states that 48 participants were included in the outcome population. The outcome description notes that 2 participants completed only the first regimen, and the regimen counts are 30, 32, and 32. A detailed participant flow account and reasons for missing regimen outcomes are not reported. The missing-data methods and formal analysis-population definition are also not reported, limiting assessment of selection and attrition effects.

The record provides mean concentrations and standard deviations, but not individual-level distributions, interval estimates for each regimen mean, or a reported test of dose proportionality. It gives no reported performance results for the proposed adherence prediction model, including predictive accuracy or validation. The posted outcome therefore describes regimen-level biomarker concentrations rather than demonstrating individual prediction performance.

The statistical analysis plan, original sample-size justification, and multiplicity handling are not reported. The recalculated planning illustrations use two-arm equal allocation assumptions and do not represent the trial’s original design assumptions. Finally, safety counts are pooled across dosing regimens, so regimen-specific safety comparisons cannot be assessed from the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Pre-Exposure Prophylaxis (PrEP) Adherence Monitoring Using Dried Blood Spots — NCT02022657.
• Registry record last updated 2019-04-30; status last verified 2019-04.
• Results first posted 2019-04-18.
• 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

The registry record describes a completed randomized, unmasked crossover study of dried-blood-spot TFV-DP concentrations under directly observed Truvada dosing at 33%, 67%, and 100% of daily dosing. It lists enrollment of 52 and identifies a primary outcome population of 48. The primary outcome is steady-state TFV-DP concentration in fmol/punch, reported as a mean and standard deviation for each regimen.

Posted regimen means are 530.0, 997.0, and 1605.0 fmol/punch, respectively. Recalculated unadjusted comparisons against the 33% regimen have p < 0.001, with confidence intervals above zero. The registry record does not report a crossover-adjusted analysis, missing-data methods, or results validating the proposed adherence prediction model. Safety information is pooled across regimens and lists 1 participant affected by a serious adverse event among 48 at risk, with 0 deaths.