A Simplification Study of Unboosted Reyataz With Epzicom (ASSURE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Simplification Study of Unboosted Reyataz With Epzicom (ASSURE) (NCT01102972), a randomized phase 4 study. The primary outcome is Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <50 Copies (c)/Milliliter (mL) at the Week 24 Visit: TLOVR Analysis.

2. Clinical Question

This was a comparison of treatment strategies in people who were already virologically suppressed, not a study of starting antiretroviral therapy in an untreated population. The intervention changed the accompanying drugs and stopped ritonavir while retaining atazanavir. The comparator continued the existing atazanavir, ritonavir, and tenofovir/emtricitabine combination. The registry’s brief summary describes the comparison over 48 weeks, while the primary endpoint is specified at Week 24.

The clinical question is therefore whether the proportion meeting the specified viral-load response definition differed between the assigned regimens at the primary assessment. The endpoint definition also counts certain events as non-response, including premature discontinuation and confirmed rebound. This makes the question about response under the stated TLOVR rules, rather than solely whether a Week 24 blood sample was below the threshold.

3. Trial Design

The registry describes a Phase 4, randomized, parallel-group, open-label study. There was no masking. The study compared two drug regimens in virologically suppressed, HIV-1 infected, HLA-B*5701 negative participants. Enrollment was 297. The registry lists the status as completed, with a start date of 2010-04 and primary completion at 2012-06.

One group changed to ATV plus ABC/3TC and discontinued pre-study RTV. The other continued pre-study ATV, RTV, and TDF/FTC without modification. Both arm descriptions specify treatment for 48 weeks. The registry describes the intervention as a simplification strategy, so the assigned regimens differed in both whether RTV was continued and which companion antiretroviral combination was used.

Random allocation is intended to create groups that are comparable, on average, with respect to factors that could affect the outcome. The record says the primary comparison was stratified by initial antiretroviral treatment. Details of the randomization sequence, allocation concealment, stratification implementation, and any other design restrictions are not reported in the registry record.

Open-label means participants and study personnel were not masked to assigned treatment. The primary endpoint is based on a laboratory measurement, but the registry does not describe whether laboratory staff were masked. The record lists 199 participants in the ABC/3TC + ATV primary-outcome arm and 97 in the TDF/FTC + ATV/RTV arm. Arm-specific counts can differ from the overall enrollment count because outcome populations and analysis records may not include every enrolled participant; the reasons for any such differences are not reported in the registry record.

The study includes a primary Week 24 endpoint and additional outcomes, including viral-load response at later visits and change from baseline in HIV-1 RNA. The registry lists 24 outcome measures and one analysis. The original sample-size justification, target enrollment calculation, planned interim analyses, and full statistical analysis plan are not reported in the registry record.

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: HLA-B\*5701-negative PAR receiving an ATV/RTV + TDF/FTC regimen QD who are virologically suppressed (plasma HIV-1 RNA \<75 c/mL) and met all eligibility requirements were randomized 2:1 to receive an ART regimen of ATV 400 mg QD + ABC/3TC 600 mg/300 mg QD (simplification arm) or ATV/RTV 300 mg/100 mg QD + TDF/FTC 300 mg/200 mg QD (continuation arm).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT)-Exposed Population: all participants exposed to at least one dose of study medication. The primary analysis method was time to loss of virologic response (TLOVR) for the proportion of participants HIV-1 RNA \<50 copies/mL at Week 24.

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 Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <50 Copies (c)/Milliliter (mL) at the Week 24 Visit: TLOVR Analysis, measured over Week 24.

The primary endpoint is the percentage of participants in the ITT-Exposed Population who achieved HIV-1 RNA below 50 copies/mL at Week 24, analyzed using time to loss of virologic response, or TLOVR. Viral load is measured from blood samples. The endpoint translates an individual laboratory result into a responder or non-responder classification under specified rules, then compares the proportion classified as responders in each treatment arm.

Under the registry’s TLOVR description, a responder had confirmed HIV RNA below 50 copies/mL and had not met a non-responder criterion. Non-response included never achieving confirmed suppression below the threshold, prematurely discontinuing the study or medication for any reason, confirmed rebound to at least 50 copies/mL, or an unconfirmed HIV RNA of at least 50 copies/mL at the last visit. Thus, the definition incorporates follow-up and discontinuation events as well as the viral-load threshold.

Using a defined endpoint makes the comparison interpretable: the reported percentage reflects the fraction meeting a common response rule, rather than a mean viral-load value. TLOVR is useful for representing sustained response and for specifying how some discontinuations or rebound events count in the analysis. It can also make the result depend on the operational rules and follow-up available, so the endpoint should be read according to that definition rather than as a direct count of only Week 24 samples below the threshold.

The registry reports this as a percentage endpoint and identifies the analysis population and method. Further details about measurement schedules, confirmation rules beyond the stated definition, and handling of other missing measurements are not reported in the registry record.

7. Results Posted in the Registry

• TDF/FTC + ATV/RTV: 86.6% (84/97) versus 86.9% (173/199) on control; risk difference -0.3 percentage points (95% CI -8.6 to 7.9), risk ratio 1.00 (0.91–1.10); unadjusted two-proportion z-test p = 0.936.

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.

Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 24 Visit: TLOVR Analysis

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • TDF/FTC + ATV/RTV: 86.6% (84/97) versus 88.4% (176/199) on control; risk difference -1.8 percentage points (95% CI -9.9 to 6.3), risk ratio 0.98 (0.89–1.07); unadjusted two-proportion z-test p = 0.649.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC + ATV/RTV and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 48 Visit: TLOVR Analysis

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • TDF/FTC + ATV/RTV: 83.5% (81/97) versus 80.9% (161/199) on control; risk difference 2.6 percentage points (95% CI -6.6 to 11.8), risk ratio 1.03 (0.92–1.15); unadjusted two-proportion z-test p = 0.587.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC + ATV/RTV and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HIV-1 RNA at Week 24

• 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:
  • TDF/FTC + ATV/RTV: mean 0.01 versus 0.01 on control; difference -0.01 (95% CI -0.09 to 0.08), standardized effect d = -0.02; z-test p = 0.887.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC + ATV/RTV and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary Week 24 assessment in several directions: viral-load response at additional thresholds and visits, different response-analysis definitions, and change from baseline in HIV-1 RNA. The posted secondary results include Week 24 and Week 48 outcomes at the 400 copies/mL threshold, along with change from baseline at Week 24. The registry lists additional outcomes, including measures at other visits and analysis definitions, but not all those results are included in the posted secondary summaries.

Across the available secondary results, the reported response percentages are broadly similar between arms, and the change-from-baseline means are close. The corresponding unadjusted intervals are wide enough to include no difference. This general pattern is compatible with the primary result’s lack of strong evidence for a difference, but secondary endpoints do not independently settle the primary question. They use different thresholds, visits, populations or analysis rules and may answer related but non-identical questions.

Multiple outcomes create a multiplicity issue: the more comparisons examined, the greater the chance that some may appear notable by chance, even if there is no underlying effect. Unless a multiplicity strategy is prespecified and applied, secondary p-values are generally less confirmatory than the primary test. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Therefore, unadjusted secondary results are best treated as supportive or exploratory context, rather than as a collection of independent confirmatory claims.

The registry lists 24 outcome measures, while the posted record identifies one analysis. Details of the full analysis plan, including which secondary findings were prioritized and how missing observations were handled for each endpoint, are not reported in the registry record. The overall pattern can be described, but it should not be converted into a broad claim that every secondary outcome was equivalent between regimens.

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

• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <50 c/mL at the Week 24 Visit: Observed, M/D=F, and SNAPSHOT Analyses
• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <50 c/mL at the Week 48 Visit: TLOVR, Observed, M/D=F, and SNAPSHOT Analyses
• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 24 Visit: TLOVR Analysis
• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 48 Visit: TLOVR Analysis
• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 24 Visit: Observed, MD=F, and SNAPSHOT Analyses
• Percentage of Participants (PAR) Who Achieved Plasma HIV-1 RNA <400 c/mL at the Week 48 Visit: Observed, MD=F, and SNAPSHOT Analyses
• Change From Baseline in HIV-1 RNA at Week 24
• Change From Baseline in HIV-1 RNA at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a randomized parallel-group comparison with an open-label design. Each participant was assigned to one of two regimens. In a randomized trial, allocation is intended to reduce systematic differences between groups at baseline, though chance imbalances can remain. The registry record does not describe the sequence-generation procedure, concealment process, or details of any stratification used during randomization.

What does the TLOVR endpoint count?

TLOVR means time to loss of virologic response. For this primary endpoint, the registry classifies participants as responders if they had confirmed HIV-1 RNA below 50 copies/mL and did not meet a non-responder rule. The listed non-response criteria include failure to achieve confirmed suppression, premature discontinuation of study or medication for any reason, confirmed rebound to at least 50 copies/mL, and an unconfirmed result at or above the threshold at the last visit. This is a composite operational definition: laboratory response and certain follow-up events both determine classification.

That construction can be useful when the scientific question concerns maintaining a virologic response rather than a single isolated measurement. It also means that different endpoint definitions can yield different response proportions from the same participants. The registry lists other analysis approaches for secondary outcomes, including observed-case and SNAPSHOT analyses, but their detailed rules are not reported in the registry record.

What does the sponsor’s comparison estimate?

The sponsor reports a Cochran-Mantel-Haenszel analysis of treatment difference in proportions, with stratification by initial antiretroviral treatment described in the primary endpoint record. This method compares proportions while accounting for the stated strata. Stratification can be useful when a factor is expected to relate to outcome or is part of the analysis plan, because it avoids treating the stratified groups as if they were unrelated to the comparison. The registry does not report the stratum-specific counts or estimates, so those contributions cannot be examined from the record.

The reported treatment difference is 0.33, with a 95% confidence interval from -7.97 to 8.64 and p = 0.937. The record does not state the unit convention for this reported difference beyond identifying it as a treatment difference of proportions. The posted recalculation instead gives an unadjusted risk difference using the arm-level summary data. An unadjusted comparison and a stratified analysis need not be numerically identical, even when they are based on the same trial, because their estimands and statistical procedures can differ.

How should a risk difference and p-value be read?

A risk difference expresses the difference between response proportions in the comparison groups, with direction determined by which arm is subtracted from which. A confidence interval describes a range of values compatible with the estimate under the statistical model and sampling assumptions. It communicates uncertainty, rather than a guarantee that the true effect lies within the interval. A p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and analysis assumptions. It is not the probability that the null hypothesis is true, nor a measure of clinical importance.

For binary outcomes, the proportion is affected by both the number of participants classified as responders and the analysis population denominator. The TLOVR rules determine the classification, while the arm-specific analysis counts determine the denominator. The registry identifies the primary population as participants who received at least one dose. It does not provide a full participant flow or explain every difference between enrollment and endpoint counts.

What does the design leave uncertain?

Open-label assignment can affect behavior, treatment management, reporting, and decisions to discontinue, even when an endpoint includes an objective laboratory measure. Randomization helps with baseline comparability but does not remove every potential source of bias after assignment. The registry does not report whether laboratory assessment was masked, how adherence was evaluated, or whether the statistical analysis plan specified sensitivity analyses.

For a non-inferiority or equivalence interpretation, the decision depends not only on the observed difference and its confidence interval but also on a prespecified margin and analysis rules. The registry identifies the sponsor analysis as non-inferiority or equivalence but does not report the margin or its justification. Thus, the statistical estimates can be described, while the formal margin-based conclusion cannot be independently assessed from the registry record.

The posted unadjusted calculations are recalculations from arm-level summaries. They are useful for understanding the direction and approximate uncertainty of a simple comparison, but they do not reproduce the stratified sponsor method. No discrepancy is recorded. The registry’s sponsor analysis remains the reported trial analysis, and the unadjusted figures should be read as a separate descriptive statistical check rather than as a replacement for it.

11. Confidence Intervals and Precision

The primary sponsor estimate is a treatment difference of proportions of 0.33, with a 95% confidence interval from -7.97 to 8.64. The unadjusted recalculation reports a risk difference of -0.003, with a 95% confidence interval from -0.086 to 0.079. The arm response percentages are 86.9% and 86.6%. Each interval includes no difference and spans values in both directions, so the data do not pinpoint a single treatment difference.

A confidence interval is a measure of statistical precision under the assumptions of the method used. A narrower interval generally indicates greater precision; a wider one indicates that a broader range of effects remains compatible with the data. The interval is not a probability statement about the fixed true effect. It also does not tell whether the interval’s full range is clinically acceptable: that requires a clinical threshold or, for a non-inferiority or equivalence conclusion, a prespecified margin. That margin is not reported in the registry record.

The sponsor and recalculated intervals arise from different procedures. The sponsor used a stratified Cochran-Mantel-Haenszel analysis, while the recalculation is an unadjusted comparison of posted summaries. They should not be treated as interchangeable estimates. The sponsor’s result is the reported trial analysis; the unadjusted interval adds a direct comparison of the arm summaries.

Precision is also shaped by the number of participants with outcome data and by the response frequency. The primary outcome arm counts are 199 and 97, and response rates are high in both groups. The registry does not provide enough information to assess all sources of uncertainty, including any effects of missing data or the details of the original design assumptions. Accordingly, the confidence intervals describe sampling uncertainty for the specified analyses, not every limitation in the evidence.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design calculation. For this binary endpoint, the figures are participants per arm, not total events. 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. The original trial’s sample-size assumptions and justification are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 158,961 participants per arm for 80% power and 212,803 participants per arm for 90% power. Planning for 75% of the observed effect gives 281,836 participants per arm for 80% power and 377,298 participants per arm for 90% power. Planning for 50% of the observed effect gives 632,415 participants per arm for 80% power and 846,623 participants per arm for 90% power.

Power is the chance, under a specified true effect and the planning assumptions, of rejecting the null hypothesis with the chosen test. The 80% and 90% columns therefore describe different target probabilities for detecting the assumed effect if it were real. A higher target power generally requires a larger planned sample. Because the observed primary effect is very small, the planning illustrations are extremely large; assuming a smaller effect makes the required sample larger still.

These figures are not observed power. They are hypothetical planning calculations based on the observed effect and stated assumptions, not a retrospective measure of how likely this completed trial was to find a difference. They also do not establish what sample size the investigators intended or whether the trial met its original design objective. The curve should be interpreted as a visual expression of the same planning relationship, not as additional trial evidence.

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 = 0.869; treatment proportion p₁ = 0.866; average p̄ = 0.868.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4792 = 0.9392.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4792 = 0.4033.
4. n = (0.9392 + 0.4033)² / (-0.0034)² = 158,960.6, rounded up to 158,961 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 <- 0.869346733668342                          # control proportion
p1 <- 0.865979381443299                          # 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(1102972)
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 = 158,961 (80% power), 212,803 (90% power)
 75% of observed effect: n per arm = 281,836 (80% power), 377,298 (90% power)
 50% of observed effect: n per arm = 632,415 (80% power), 846,623 (90% power)
power.prop.test: 158960.6 
Simulated power at n = 158,961 per arm: 0.804 (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 sponsor’s own primary analysis reports a Cochran-Mantel-Haenszel treatment difference of proportions of 0.33, with a 95% confidence interval from -7.97 to 8.64 and p = 0.937. It stratified by initial antiretroviral treatment, as stated in the primary endpoint description. This is the inferential result reported for the trial.

The posted recalculation uses the two arm-level response summaries to form an unadjusted risk difference of -0.003, with a 95% confidence interval from -0.086 to 0.079 and an unadjusted p-value of 0.936. It does not reproduce the sponsor’s stratification. The arm rates are close, and the two p-values are also close, but the estimates use different analysis descriptions and should be read as distinct outputs.

No discrepancy is recorded between the posted summaries and reported analysis. The recalculation is therefore best treated as a transparent unadjusted check, not a correction to the sponsor’s analysis. The reported sponsor estimate takes precedence as the trial’s own analysis. The registry does not report the non-inferiority or equivalence margin, so the numerical result alone cannot establish whether a formal margin-based criterion was satisfied.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is clearly identified, but the registry does not report a complete statistical analysis plan or a multiplicity-control strategy for the many listed outcomes and analysis definitions. When several endpoints, time points, thresholds, or analysis methods are examined, chance alone can produce apparently unusual results in some comparisons. Adjusting for multiplicity or setting a prespecified testing hierarchy can limit that problem. Without a reported strategy, secondary p-values should be interpreted cautiously and should not carry the same confirmatory weight as the primary analysis.

The primary analysis population is the ITT-Exposed Population, defined as participants exposed to at least one dose of study medication. This is not the same as every enrolled participant by definition. The registry provides primary-outcome counts by arm but does not report a full flow of enrolled, randomized, treated, followed, and analyzed participants, or explain all differences between those counts. The exact handling of participants with missing Week 24 measurements, beyond the stated TLOVR non-responder rules, is not reported in the registry record.

TLOVR counts premature study or medication discontinuation as non-response and includes specified rebound and last-visit criteria. These rules reduce reliance on treating all missing outcomes as if they were successful responses, but they do not remove every concern about missing data. The interpretation can depend on why participants discontinued, whether follow-up differed between arms, and whether missing observations were associated with outcome. Reasons for discontinuation and sensitivity analyses addressing missing data are not reported in the registry record.

The trial is open-label. Knowledge of assigned treatment can influence participant behavior, clinical management, and discontinuation decisions. The primary endpoint uses laboratory viral-load results, which are more objective than a subjective rating, but the registry does not say whether laboratory assessment or outcome classification was masked. It also does not describe adherence measurement or other protections against post-randomization bias.

The registry identifies a non-inferiority or equivalence analysis but does not report the margin, its clinical justification, or the planned decision rule. It also does not report interim analyses or the original sample-size justification. These absences limit independent assessment of the analysis plan and of how the reported result was intended to support a formal claim.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cellulitis (1.5%), gastroenteritis shigella (1.0%), hepatitis c (1.0%), abdominal pain (1.0%), colon cancer (1.0%).

The registry reports serious adverse events in 21 of 199 participants in the ABC/3TC + ATV group and 6 of 97 participants in the TDF/FTC + ATV/RTV group. Other adverse events are reported for 92 of 199 and 31 of 97 participants, respectively. These counts describe the event categories as recorded; the registry summary does not provide a comparative statistical analysis for these figures.

The listed serious adverse event terms include cellulitis at 1.5%, gastroenteritis shigella at 1.0%, hepatitis C at 1.0%, abdominal pain at 1.0%, colon cancer at 1.0%, and chest pain at 1.0%. These terms are presented as the top serious-event listings, not as a complete account of every event or as evidence that treatment caused them. The registry does not provide event-level timing, duration, outcome, or attribution in the information.

Serious adverse event counts should be read alongside the number at risk and the study’s follow-up, rather than as a simple measure of comparative safety. The registry record does not report deaths for these groups. The figures alone do not establish that one regimen is safer or less safe, and they do not replace clinical assessment of the full safety record.

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

The posted results describe a randomized comparison in which the Week 24 TLOVR response percentages were 86.9% for ABC/3TC + ATV and 86.6% for TDF/FTC + ATV/RTV. The sponsor’s stratified analysis estimates a treatment difference of 0.33 and reports a confidence interval from -7.97 to 8.64. The unadjusted recalculation also has an interval that spans differences in either direction. The data therefore do not identify a precise difference between these regimens for the specified outcome.

That interpretation is not the same as proving the regimens are identical. A result that does not show strong evidence of a difference can reflect genuinely similar outcomes, limited precision, or both. For a formal non-inferiority or equivalence conclusion, the estimate must be judged against a prespecified margin and analysis plan. The margin is not reported in the registry record, so the formal status of such a conclusion cannot be assessed from the reported estimates alone.

The endpoint is specifically the TLOVR classification at Week 24 among participants exposed to at least one dose. Its rules count certain discontinuations and rebound events as non-response. The result should not be generalized automatically to outcomes defined by a different viral-load threshold, a different visit, an observed-case analysis, or a different population. Nor does it by itself characterize long-term outcomes beyond the period described by the study.

The registry reports serious and other adverse-event counts, but those summaries do not establish causation or provide a complete comparative safety assessment. The record also does not provide the full participant flow, detailed missing-data sensitivity analyses, the original sample-size justification, or the non-inferiority margin. Those limitations matter when deciding how much certainty to place in broader interpretations.

In statistical terms, the central result is a close pair of observed response percentages with uncertainty that includes no difference. It supports a cautious description of the observed data, not a claim that every possible clinically relevant difference has been ruled out.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary question concerns a treatment simplification strategy in participants already virologically suppressed. The endpoint is not simply a single viral-load measurement: TLOVR incorporates confirmation, rebound, and specified discontinuation events into a responder definition. Understanding those rules is necessary before interpreting the response percentages.

It also illustrates the distinction between a sponsor-reported stratified analysis and a simple unadjusted recalculation from arm summaries. Both describe the same broad comparison, but they are not interchangeable estimates. The sponsor analysis is the trial’s own inferential result, while the recalculation helps readers see how a direct comparison of the posted proportions behaves. Their close p-values do not make their methods identical.

The registry labels the analysis as non-inferiority or equivalence, yet does not report the margin needed to judge a formal claim. This is an important reporting limitation: a small observed difference and a non-significant test do not by themselves establish equivalence. Confidence intervals, margins, endpoint definitions, and analysis populations all contribute to that judgment.

The record also lists many outcomes and analysis approaches. This highlights why multiplicity and a prespecified hierarchy matter: secondary results can enrich interpretation but should not be treated as a set of independent confirmations when adjustment and prioritization are not documented. Finally, planning illustrations based on the observed effect are not the same as the original design calculation or observed power. Keeping these distinctions clear helps prevent descriptive similarities from being overstated as definitive proof.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry does not report the non-inferiority or equivalence margin, its justification, or the decision rule. This prevents an independent margin-based assessment of the primary result. The original sample-size justification and design assumptions are also not reported, so the posted planning illustrations cannot be used to reconstruct the investigators’ intended operating characteristics.

The record does not provide a full participant flow or explain all differences between enrollment and the arm counts used for the primary outcome. Although TLOVR specifies several non-response criteria, further handling of missing Week 24 measurements and sensitivity analyses are not reported. The results may therefore be difficult to assess under alternative assumptions about incomplete follow-up.

The study was open-label, and masking of laboratory assessment is not reported. The primary outcome uses a laboratory measurement, but treatment knowledge could still influence adherence, clinical decisions, or discontinuation. The registry does not provide detailed adherence results, reasons for discontinuation, or stratum-specific outcome summaries for the sponsor’s analysis.

Multiple secondary outcomes and analysis definitions are listed, but a multiplicity strategy and complete analysis hierarchy are not reported. Only some secondary results are summarized in the posted data. The available secondary findings consequently provide limited context and should not be treated as a complete confirmatory evaluation.

Safety information is also summary-level: the registry gives counts and selected serious-event terms but not a full event-level account, comparative inference, attribution, or deaths. These limitations do not invalidate the reported estimates; they define what can be concluded from the registry record and what remains uncertain.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Simplification Study of Unboosted Reyataz With Epzicom (ASSURE) — NCT01102972.
• Registry record last updated 2013-11-19; status last verified 2013-09.
• Results first posted 2012-12-31.
• 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

NCT01102972 is a completed Phase 4 randomized, parallel-group, open-label study comparing ABC/3TC + ATV with continued TDF/FTC + ATV/RTV in virologically suppressed, HIV-1 infected, HLA-B*5701 negative participants. Enrollment was 297. The primary endpoint was the Week 24 percentage with HIV-1 RNA below 50 copies/mL using TLOVR in the ITT-Exposed Population.

The registry reports response percentages of 86.9% and 86.6%. The sponsor’s Cochran-Mantel-Haenszel analysis reports a treatment difference of 0.33, a 95% confidence interval from -7.97 to 8.64, and p = 0.937. The unadjusted recalculation is similar in broad interpretation but is not the sponsor’s stratified analysis. The non-inferiority or equivalence margin, multiplicity plan, original sample-size justification, and further missing-data details are not reported in the registry record.