Safety and Acceptability Study of Oral Emtricitabine/Tenofovir Disoproxil Fumarate Tablet and Rectally-Applied Tenofovir Reduced-Glycerin 1% Gel: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Acceptability Study of Oral Emtricitabine/Tenofovir Disoproxil Fumarate Tablet and Rectally-Applied Tenofovir Reduced-Glycerin 1% Gel (NCT01687218), a randomized phase 2 study. The primary outcome is Safety: Grade 2 or Higher Adverse Events.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, open-label crossover study with six sequences and three product-use periods. The registry describes a multisite study and lists HIV as the condition. Enrollment was 195. The study status is completed; the recorded start date is 2013-09-25 and the primary completion date is 2015-05-26.

Each product-use period lasted 8 weeks, with a 1-week washout between periods, for a stated timeframe of 27 weeks. Participants were assigned to sequences that varied the order of daily oral emtricitabine/tenofovir disoproxil fumarate, daily rectal tenofovir reduced-glycerin 1% gel, and rectal gel associated with receptive anal intercourse. The sequence structure means regimen comparisons arise within a study in which treatment order varied; the record does not describe a parallel design in which each participant stayed on only one regimen.

Masking was none, so the study was open label. Participants and study personnel were not masked to the assigned regimen according to the registry design entry. Randomization of sequence can help distribute order assignments, but it does not itself mask treatment or establish that every possible source of bias was controlled. Further details of randomization procedures, sequence balance, and any period or carryover effects are not reported in the registry record.

The main outcome was the number of participants with grade 2 or higher adverse events. The registry says the primary analysis used evaluable participants under an intent-to-treat principle, including randomized participants regardless of whether they received product in a given period. It also notes an exception for the oral regimen period when a participant ended participation before that period’s initiation visit. The study measured pharmacokinetic outcomes as well, including concentrations in blood plasma, rectal tissue, and rectal sponge, and listed adherence outcomes. Numerical results for all listed secondary measures are not reported in the registry record.

The registry does not report the original sample-size justification or the assumptions used to plan the trial. Planning illustrations based on observed effects are a separate exercise and should not be treated as the trial’s original design rationale.

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: 349 persons were screened and 154 were excluded for various reasons. The study enrolled 195 participants, 187 of whom are evaluable. Evaluable participants are those participants who were enrolled and not replaced, or were the final enrolled replacement participant for another enrolled participant who met the criteria for replacement.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Among the 187 evaluable participants. One participant was terminated before the Initiate Period visit of his/her Period 3 (Oral Tablet regimen period). Thus, this participant is removed from the analysis of the oral period 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: Includes all participants enrolled.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Safety: Grade 2 or Higher Adverse Events, measured over 27 weeks (three 8-week product use periods with 1-week washout periods between them).

The primary endpoint is the number of participants with at least one grade 2 or higher adverse event during the study’s stated 27-week timeframe. The registry frames this outcome as a comparison of the safety profiles of daily oral FTC/TDF, daily rectal TFV RG 1% gel, and RAI-associated rectal TFV RG 1% gel. The analysis description says the endpoint was assessed among evaluable participants under an intent-to-treat principle, with randomized participants included whether or not they received product in a given period.

A participant count is useful because it records how many people experienced an event meeting the specified severity threshold. It is not the same as a count of every event: a participant may have more than one event, while the endpoint may count that participant once. The posted primary outcome does not describe event timing, recurrence, duration, or severity distributions beyond the grade threshold. Those details are not reported in the registry record.

Safety is relevant to a comparison of regimens because unwanted events are an important outcome in studies of products intended for prevention. The endpoint captures only the defined grade 2 or higher threshold and cannot, by itself, describe all aspects of acceptability, adherence, drug exposure, or safety. The registry also lists serious adverse events separately, and those figures should be read as a distinct safety summary rather than as a substitute for the primary endpoint.

In general, a safety endpoint is most informative when its definition, observation period, analysis population, and handling of incomplete follow-up are clear. The record states the endpoint threshold and timeframe and gives some analysis-population information, but additional details about missing observations and event adjudication are not reported in the registry record.

7. Results Posted in the Registry

• Product 2: 32.6% (61/187) versus 34.4% (64/186) on control; risk difference -1.8 percentage points (95% CI -11.4 to 7.8), risk ratio 0.95 (0.71–1.26); unadjusted two-proportion z-test p = 0.714.
• Product 3: 29.9% (56/187) versus 34.4% (64/186) on control; risk difference -4.5 percentage points (95% CI -13.9 to 5.0), risk ratio 0.87 (0.65–1.17); unadjusted two-proportion z-test p = 0.356.

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.

Pharmacokinetics: End Period Tenofovir (TFV) Concentrations (log10 ng/mg) in Rectal Tissue

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Product 2: mean 0.84 versus 0.18 on control; difference 0.66 (95% CI 0.43 to 0.89), standardized effect d = 1.31; z-test p = <0.001.
  • Product 3: mean 0.02 versus 0.18 on control; difference -0.16 (95% CI -0.49 to 0.17), standardized effect d = -0.22; z-test p = 0.341.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Product 2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Product 3 and the control. The interval gives the range of effects that remain compatible with the data.

Pharmacokinetics: End Period Emtricitabine (FTC) Concentrations (log10 ng/mg) in Rectal Tissue

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Product 2: mean -1.26 versus -0.35 on control; difference -0.91 (95% CI -1.02 to -0.80), standardized effect d = -3.90; z-test p = <0.001.
  • Product 3: mean -1.26 versus -0.35 on control; difference -0.91 (95% CI -1.02 to -0.80), standardized effect d = -3.90; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Product 2 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 mean is statistically lower for Product 3 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Pharmacokinetics: End Period Tenofovir-Diphosphate (TFV-DP) Concentrations (log10 ng/mg) in Rectal Tissue

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Product 2: mean 2.06 versus 1.52 on control; difference 0.54 (95% CI 0.30 to 0.78), standardized effect d = 1.06; z-test p = <0.001.
  • Product 3: mean 1.54 versus 1.52 on control; difference 0.02 (95% CI -0.32 to 0.36), standardized effect d = 0.03; z-test p = 0.909.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Product 2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Product 3 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study beyond participant-level adverse events. The registry lists pharmacokinetic measurements of tenofovir and emtricitabine in plasma, rectal tissue, and rectal sponge, tenofovir-diphosphate in rectal tissue, and adherence over an 8-week period. These outcomes address drug exposure and product use, not the primary safety endpoint. Concentration measurements can show whether exposure differs by regimen, but they do not by themselves demonstrate prevention benefit or establish how a participant will experience a product.

The posted tissue summaries show that concentration contrasts depend on the analyte and the comparison. Some comparisons have estimates and confidence intervals suggesting a clearer separation, while others are less precise and include values compatible with little or no difference. This overall pattern is not a single uniform result across all pharmacokinetic outcomes. The measurements were based on a subset of participants, and their interpretation depends on the specified compartment, transformed measurement scale, sampling period, and analysis method.

The registry lists eight secondary outcomes, but numerical findings for plasma, rectal sponge, and adherence measures are not reported in the registry record. Those outcomes should not be described as showing a particular level or pattern when the numerical results are unavailable. The reported secondary results also do not alter the interpretation of the primary safety comparison: evidence about concentration is distinct from evidence about adverse-event occurrence.

Secondary analyses are often less definitive than a single prespecified primary analysis when many outcomes and comparisons are examined. In general, making multiple comparisons increases the opportunity to observe apparently notable findings by chance if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity adjustment or a testing hierarchy. Accordingly, individual secondary p-values and intervals should be read as exploratory or supportive evidence unless additional prespecification and multiplicity information is available. The pharmacokinetic findings are useful for describing measured exposure, but their statistical signals should not be treated as independent confirmations of a safety effect.

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

• Pharmacokinetics: Tenofovir (TFV) Concentrations (log10 ng/mL) in Blood Plasma
• Pharmacokinetics: End Period Tenofovir (TFV) Concentrations (log10 ng/mg) in Rectal Tissue
• Pharmacokinetics: Tenofovir (TFV) Concentrations (log10 ng/mg) in Rectal Sponge
• Pharmacokinetics: Emtricitabine (FTC) Concentrations (log10 ng/mL) in Blood Plasma
• Pharmacokinetics: End Period Emtricitabine (FTC) Concentrations (log10 ng/mg) in Rectal Tissue
• Pharmacokinetics: Emtricitabine (FTC) Concentrations (log10 ng/mg) in Rectal Sponge
• Pharmacokinetics: End Period Tenofovir-Diphosphate (TFV-DP) Concentrations (log10 ng/mg) in Rectal Tissue
• Adherence: Percentage of Prescribed Doses Taken Orally or Administered Rectally in an 8-week Period

9. Statistical Interpretation

10. Statistical Methods Explained

The study randomized participants to sequences of regimens, rather than assigning each participant to a single regimen for the whole study. In a crossover design, participants receive multiple regimens over successive periods. This can make within-participant comparisons informative because observations from the same person may be related. It also makes treatment order and period relevant: a participant’s outcome in one period could depend on the period, prior exposure, or other time-related factors. The record identifies a crossover design but does not report detailed methods for evaluating period or carryover effects.

What does the primary risk difference represent?

The simple recalculations express the comparison as a risk difference: the estimated event proportion for one product label minus the estimate for Product 1. A value below zero means the observed proportion for the compared label is lower in the unadjusted calculation; a value above zero would mean it is higher. This is a descriptive, unadjusted contrast based on posted counts. It does not account for within-participant dependence across crossover periods, sequence, or any model covariates. Therefore, it should be distinguished from the sponsor’s analysis.

For a binary outcome, a risk ratio instead compares event proportions as a ratio. The registry reports sponsor analyses using generalized estimating equations, with risk ratios as the parameter. In general, generalized estimating equations can account for correlation among repeated observations from the same participant while estimating an average association across the study population. The registry does not state the full model specification, working correlation structure, covariates, or other implementation details, so those should not be inferred from the method name alone.

A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it quantify the probability that a result is due to chance. The sponsor-reported p-values are attached to the model-based comparisons; the recalculated p-values are simple unadjusted analyses from posted summary statistics. A p-value should be read alongside the estimated effect and its interval, not as a standalone measure of importance.

How should the continuous outcomes be read?

The selected tissue pharmacokinetic outcomes are reported as means with standard deviations. A mean describes the average measured concentration in the specified outcome group. A standard deviation describes the spread of individual measurements around that average; it is not the uncertainty interval for the mean. The outcomes use log10 concentration units, so the reported means refer to the transformed scale identified in the registry. Interpretation on that scale differs from reading a mean concentration in the original units.

The simple recalculations give mean differences and confidence intervals from the posted summary statistics. A mean difference is the estimated average for one product label minus the average for Product 1. These recalculations do not reproduce the sponsor’s reported mixed models analysis, which reports a slope estimate and confidence interval. In general, mixed models can represent repeated measurements and account for correlation within participants, but the record does not provide enough model details to describe its precise structure or assumptions.

For the tenofovir tissue outcome, the recalculated comparison of Product 1 with Product 2 has a mean difference of 0.66 and a 95% confidence interval from 0.427 to 0.893; the sponsor reports a slope of 0.66 with a 95% confidence interval from 0.49 to 0.83. For the Product 1 versus Product 3 comparison, the recalculated mean difference is -0.16 with a 95% confidence interval from -0.489 to 0.169; the sponsor reports a slope of -0.16 with a 95% confidence interval from -0.46 to 0.15. These estimates are on the stated log10 concentration scale.

For the emtricitabine tissue outcome, the recalculated mean difference is -0.91 for each comparison with Product 1, and the unadjusted intervals are below zero. The sponsor’s mixed-model results also report -0.91 for each comparison, with 95% confidence intervals from -1.01 to -0.80. The displayed means for Product 2 and Product 3 have a standard deviation of 0.0 in the posted summaries. That feature cautions against treating a simple summary-statistic calculation as a complete account of the underlying measurement distribution or model fit. Details about measurement precision, censoring, or handling of values at limits are not reported in the registry record.

For tenofovir-diphosphate, the posted comparison of Product 1 with Product 2 has a recalculated mean difference of 0.54, while the comparison with Product 3 is close to zero. The sponsor reports mixed-model slopes of 0.54 and 0.01, respectively. The respective model-based intervals and p-values are reported with the secondary results. These comparisons concern tissue drug concentration, not clinical infection outcomes.

Why distinguish recalculations from sponsor analyses?

The recalculations are unadjusted and rely only on posted summary statistics. They are useful for a transparent check of direction and approximate magnitude, but do not substitute for an analysis that uses the crossover structure or participant-level observations. The sponsor’s reported model-based analyses take precedence as the registry’s own inferential results. The registry marks no discrepancy between those reports and the recalculated summaries. Agreement in point estimates does not make the methods identical: standard errors, confidence intervals, and p-values can differ because the analytical approach and information used differ.

In general, repeated-measures methods are useful when observations from the same participant are correlated; ignoring that correlation can misstate uncertainty. But a method label is not a guarantee that every design feature has been adequately addressed. Without the full specification, assumptions, diagnostics, and missing-data procedures, the registry record supports interpretation of the reported estimates but not a complete independent audit of the statistical analysis.

11. Confidence Intervals and Precision

A confidence interval describes a range of values reasonably compatible with the data and the model used to calculate it. In repeated studies under the same assumptions, intervals formed by a 95% procedure would cover the target parameter in 95% of such studies. This is a general interpretation of the confidence level, not a statement that there is a 95% probability that a particular fixed parameter lies inside the interval.

For the primary safety comparisons, the simple risk-difference intervals are -0.114 to 0.078 for Product 2 versus Product 1 and -0.139 to 0.050 for Product 3 versus Product 1. Each interval includes zero, the value corresponding to no difference on the risk-difference scale. Their breadth indicates that the posted counts do not pinpoint a narrow range of possible differences. The sponsor’s risk-ratio intervals also include 1: 0.73 to 1.44 for Product 2 versus Product 1, and 0.64 to 1.21 for Product 3 versus Product 1. On the ratio scale, 1 is the value corresponding to equal event proportions.

For the selected secondary outcomes, interval widths vary. Some tissue concentration comparisons have intervals that do not include zero, while other comparisons do include zero. A narrow interval generally indicates greater precision for the estimated contrast under the model; it does not by itself establish clinical importance. A wider interval leaves more uncertainty about the size and possibly the direction of an effect. The tissue outcomes are based on 36 measurements per product label in the posted summaries, so their precision and applicability should be considered separately from those of the primary safety analysis.

In general, confidence intervals reflect sampling variability and the assumptions of the statistical method. They do not automatically account for unreported sources of bias, incomplete outcome data, or multiple comparisons. Nor does an interval that includes a null value establish equivalence. The registry record does not report an equivalence margin or a precision target for the original design.

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 illustrations express the number of participants per arm for 80% power and for 90% power. They are not total study enrollment figures. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. These are planning assumptions for the illustration; the assumptions used in the trial’s original design are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% column describes the corresponding target with a higher chance of detecting that effect. Greater power generally requires more participants when other planning choices remain unchanged. The values are scenario calculations, not a claim about the study’s achieved ability to detect an effect.

Rows describing 100%, 75%, or 50% of the observed effect ask what planning would look like if the target effect were the full observed estimate or a smaller fraction of it. Smaller effects are harder to distinguish from random variation and therefore require more participants. This pattern is especially important when an observed effect is uncertain: treating a noisy observed estimate as the expected true effect can make a planning illustration misleadingly optimistic or otherwise unstable.

These figures are not observed power. Observed power calculated from the effect estimated in a completed study adds little information beyond the estimate and its uncertainty. The illustrations are best read as conditional planning examples, not as evidence that the trial was adequately powered, inadequately powered, or designed around these particular effects. For time-to-event outcomes, the stated convention would be total events; the outcomes addressed by these illustrations are not time-to-event outcomes, so the displayed planning figures refer to participants per arm.

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 = 0.344; treatment proportion p₁ = 0.326; average p̄ = 0.335.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6676 = 1.3084.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6674 = 0.5617.
4. n = (1.3084 + 0.5617)² / (-0.0179)² = 10,936.5, rounded up to 10,937 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 <- 0.344086021505376                          # control proportion
p1 <- 0.32620320855615                          # 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(1687218)
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 = 10,937 (80% power), 14,641 (90% power)
 75% of observed effect: n per arm = 19,508 (80% power), 26,115 (90% power)
 50% of observed effect: n per arm = 44,036 (80% power), 58,950 (90% power)
power.prop.test: 10936.5 
Simulated power at n = 10,937 per arm: 0.802 (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. Analyses Reported by the Sponsor

The registry reports sponsor analyses for the primary safety comparisons using generalized estimating equations and risk ratios. The sponsor reports a risk ratio of 1.03, with a 95% confidence interval from 0.73 to 1.44 and p = 0.88, for Product 2 versus Product 1. For Product 3 versus Product 1, the reported risk ratio is 0.88, with a 95% confidence interval from 0.64 to 1.21 and p = 0.43. These are the registry’s own model-based results and should be the main inferential estimates when describing the sponsor’s analysis.

The simple recalculations use posted event counts to estimate unadjusted risk differences. They do not reproduce the sponsor’s repeated-measures model or use its participant-level data. The recalculated estimates and intervals can serve as a transparent descriptive comparison, but should not be substituted for the sponsor’s reported model. The registry indicates no discrepancy, and the direction of the primary point estimates is broadly consistent across these summaries; however, risk differences and risk ratios are different measures and should not be compared as if they shared a scale.

For the selected continuous secondary outcomes, the sponsor reports mixed models analysis, expressed as slopes. The recalculated mean differences generally align with the reported point estimates, but the calculations are based on summary statistics and are not the same model. In general, model-based analyses may incorporate repeated observations and account for within-participant correlation, whereas unadjusted recalculations cannot reproduce those features. Full model specifications and diagnostics are not reported in the registry record, so the reported results can be described but not fully reconstructed from the posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

The study has a primary safety endpoint and multiple secondary outcomes, and several product comparisons are reported. The registry record does not report whether the statistical analysis plan controlled the family-wise error rate, used a hierarchical testing strategy, or applied another multiplicity procedure. It also does not report whether the secondary analyses were designated as confirmatory or exploratory. Without that information, nominal p-values across several outcomes should not be interpreted as if they came from a single isolated test.

Multiplicity matters because the more comparisons examined, the greater the chance that at least one result may appear unusual under a setting where there is no true difference. In general, adjustments or a prespecified testing sequence can help control that risk, but they may also affect precision and the threshold for declaring statistical evidence. No particular adjustment should be assumed for this trial. The sponsor-reported p-values and confidence intervals should therefore be read as reported, with the missing multiplicity context in mind.

The primary analysis description says that randomized participants were included under an intent-to-treat principle regardless of whether they received product in a given period, including those lost to follow-up, terminated early, or on product hold. It describes the population as 187 evaluable participants and notes that one participant was terminated before the initiation visit of the oral regimen period; that participant was removed from the oral-period analysis. The posted primary counts show 186 for Product 1 and 187 for each of Product 2 and Product 3. The registry does not give a complete account of participant flow by period or explain how all incomplete observations were handled.

Missing-data methods are not reported in the registry record. This leaves uncertainty about whether outcome availability differed by regimen, sequence, or participant characteristics, and whether any imputation or other adjustment was used. In general, missingness can affect interpretation if the probability of an observed outcome is related to the outcome itself or to factors associated with it. The available record does not establish that missing data were absent or that they could not influence estimates.

Interim analyses, stopping rules, and the original statistical plan are also not reported in the registry record. This absence does not establish that such procedures were or were not used; it means their role cannot be assessed from the registry information. Further protocol and analysis-plan detail would be needed to evaluate prespecification, multiplicity control, and the handling of incomplete data.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalisation (0.5%), appendicitis (0.5%), suicide attempt (0.5%).

The serious adverse event summary reports 1 affected participant among 192 at risk for Product 1, 2 among 192 for Product 2, and 0 among 191 for Product 3. These are serious-event counts, distinct from the primary endpoint’s broader grade 2 or higher adverse-event counts. A count of participants affected is not necessarily a count of all serious events, and the posted summary does not give event timing or recurrence by participant.

The registry lists hospitalisation, appendicitis, and suicide attempt among the most frequent serious-event terms, each at 0.5%. The summaries do not establish that these events were caused by a study product. Causal attribution, event narratives, and the basis for classifying relatedness are not reported in the registry record. The death fields have no reported values, so deaths are not reported in the registry record.

These figures are descriptive. With low counts, estimates of comparative risk can be imprecise, and a small observed count should not be read as proof that serious events cannot occur. The serious-event summary also does not answer the broader primary question about grade 2 or higher events. Any interpretation should keep the event definition, risk-set counts, and analysis population distinct.

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

The posted results describe event counts and measured concentrations in a randomized, open-label crossover study. For the primary safety endpoint, the unadjusted comparisons and sponsor-reported risk-ratio analyses do not show a clear statistical separation between the product labels. The uncertainty intervals include the respective null values, and the estimates leave room for a range of possible differences. That is not evidence that the regimens are identical, nor does it establish that any difference is clinically important.

The secondary tissue measurements indicate that some drug-concentration comparisons differ more clearly than others. Those results describe pharmacokinetic exposure in the measured compartment, not prevention effectiveness, and should not be used to infer an effect on HIV acquisition. Numerical outcomes for several listed secondary measures are not reported in the registry record, including adherence findings. The absence of those numerical summaries limits the conclusions that can be drawn about how consistently participants used the regimens or how exposure varied across all measured compartments.

The trial’s results apply most directly to its described study population, regimens, sequence structure, and observation period. The open-label crossover design provides comparisons across different product-use periods, but the registry does not report enough detail to assess possible period effects, carryover, or all sources of incomplete follow-up. The primary analysis population is described as evaluable, with an exception for the oral period, so the exact interpretation depends on the posted analysis population for each outcome.

In general, statistical significance and clinical importance are different questions. A p-value does not measure the size or value of a difference, and a confidence interval does not settle whether a difference matters in practice. The registry record does not report thresholds for clinically meaningful differences, equivalence margins, or the original sample-size rationale. The results therefore support a cautious description of observed comparisons and their precision, not a claim of equivalence, definitive safety ranking, or treatment effectiveness.

No clinical recommendation follows from these results alone. The record reports study observations and statistical analyses; it does not establish how an individual should choose or use a product. Interpretation alongside other evidence would require information beyond the registry outcomes.

18. Why This Trial Matters Statistically

This study illustrates why clinical comparisons need to be interpreted in light of their design and analysis, not just the observed counts. A crossover trial exposes participants to multiple regimens over time, which can support within-participant comparisons but also requires attention to repeated observations, treatment sequence, and period effects. The sponsor’s use of generalized estimating equations for the primary comparisons is relevant to the repeated-measures setting, while the simple recalculations are intentionally unadjusted and cannot represent that full structure.

It also shows the value of separating an event endpoint from pharmacokinetic measurements. Adverse-event counts describe participants who experienced events under a defined severity threshold. Tissue drug concentrations describe measured exposure in a particular biological compartment. Both are informative, but they answer different questions. A concentration difference cannot be treated as a safety difference or as evidence of prevention effectiveness.

The record also demonstrates that an estimate without precision information is incomplete. The confidence intervals show how uncertain the comparisons remain, while the p-values alone cannot communicate the possible range or practical relevance of an effect. Likewise, a planning illustration derived from an observed estimate is not evidence of observed power or proof of the original design’s adequacy.

Finally, the registry contains useful limits on what can be concluded: the study was open label, the primary population is described as evaluable, secondary results are not numerically reported for every listed outcome, and multiplicity and missing-data procedures are not reported. Making these gaps explicit is part of statistical interpretation. It prevents a descriptive finding from being stretched into a stronger claim than the available analysis supports.

19. 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 trial was open label, so assignment was not masked. In general, knowledge of regimen can affect participant reporting, adherence, or study assessments, particularly for outcomes with a subjective component. The registry record does not quantify whether this occurred or describe measures used to reduce such influence. The randomized sequence design addresses allocation order but does not remove the possible consequences of unmasked treatment.

The crossover structure creates interpretive considerations beyond those in a simple parallel comparison. Outcomes can be influenced by period, order, or exposure in an earlier period. The registry record does not report detailed analyses of period effects, sequence effects, or carryover, nor does it provide enough information to assess how the washout periods performed for each outcome. These considerations are especially relevant when interpreting repeated safety observations and pharmacokinetic measures.

The primary analysis is described as involving evaluable participants, with a stated exception for one participant who did not reach the oral-period initiation visit. The registry does not provide full flow information by period or detailed missing-data methods. Consequently, the degree to which the posted analyses represent all randomized participants for each regimen cannot be independently assessed from the record. The reported enrollment of 195 and primary evaluable population of 187 refer to different stages or analysis definitions and should not be treated as interchangeable.

Selected tissue pharmacokinetic summaries use 36 measurements per product label. This smaller measurement subset limits precision and may not represent the full primary safety population. The record does not report why measurements were unavailable for other participants, whether availability differed by regimen, or how values below measurement limits were handled. For the emtricitabine tissue summaries, the reported standard deviations for Product 2 and Product 3 are 0.0; the registry does not provide enough detail to determine how that feature arose.

Only selected secondary numerical summaries are available in the information reported for these outcomes. Plasma, rectal sponge, and adherence results are not reported in the registry record. The original sample-size justification, multiplicity control, interim analyses, and complete statistical plan are also not reported. These gaps constrain assessment of prespecification and the robustness of the secondary findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Acceptability Study of Oral Emtricitabine/Tenofovir Disoproxil Fumarate Tablet and Rectally-Applied Tenofovir Reduced-Glycerin 1% Gel — NCT01687218.
• Registry record last updated 2021-06-24; status last verified 2021-06.
• Results first posted 2017-02-01.
• 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.

23. Record Summary

NCT01687218 is a completed Phase 2 randomized, open-label crossover study sponsored by CONRAD. It enrolled 195 participants and compared three regimens involving oral FTC/TDF and rectally applied tenofovir reduced-glycerin 1% gel over three 8-week product-use periods with 1-week washouts. The primary outcome was the number of participants with grade 2 or higher adverse events over 27 weeks.

The registry reports sponsor analyses of the primary safety comparisons using generalized estimating equations and risk ratios. Their confidence intervals include the null value. Simple unadjusted recalculations from posted counts provide a complementary descriptive view but do not reproduce the sponsor’s model. Selected tissue pharmacokinetic results show varying patterns across analytes and comparisons; numerical results for several listed secondary outcomes are not reported in the registry record.

Interpretation is limited by the open-label crossover design, incomplete reporting of missing-data and multiplicity procedures, and the absence of the original sample-size rationale and detailed model specifications. The results describe study observations and uncertainty, not proof of equivalence or effectiveness.