Atazanavir/Ritonavir, Once Daily + Raltegravir, Twice Daily, Switch Study in HIV-1-Infected Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Atazanavir/Ritonavir, Once Daily + Raltegravir, Twice Daily, Switch Study in HIV-1-Infected Patients (NCT01332227), a randomized phase 4 study. The primary outcome is Percentage of Participants With HIV-1 RNA Level <40 c/mL at Week 24.

2. Clinical Question

This was a phase 4 study with randomized allocation and a parallel-group design. It was open-label, with no masking reported. Enrollment was 132. The posted Week 24 analysis gives arm denominators of 72 and 37, so the enrollment figure should not be mistaken for the number contributing to that endpoint. The registry record does not explain the difference between the overall enrollment and the endpoint denominators.

3. Trial Design

The study evaluated a switch from a regimen of two nucleoside reverse transcriptase inhibitors plus another agent to one of two regimens. Participants were described as virologically suppressed and as having safety and/or tolerability issues on their existing treatment. The randomized groups received atazanavir/ritonavir plus raltegravir or atazanavir/ritonavir plus tenofovir/emtricitabine. The latter was designated the reference regimen.

The registry classifies the study as phase 4, randomized, open-label, and parallel-group. In a parallel design, participants are assigned to one group and outcomes are compared across groups; the registry does not describe a crossover between study regimens. Because masking was absent, participants and study personnel could know which regimen was assigned. The record does not describe measures intended to limit the influence of that knowledge on outcome assessment.

Enrollment was 132. The study start is recorded as 2011-10, primary completion as 2013-09, and status as completed. The record names Bristol-Myers Squibb as sponsor. It describes an HIV-1 RNA assay and an intent-to-treat response algorithm for the primary endpoint. The endpoint population statement and the algorithm's description of the denominator do not use identical wording, and the registry record does not reconcile them.

The planned outcomes extended beyond the primary Week 24 suppression measure. They included suppression at Week 48, virologic rebound at Weeks 24 and 48, resistance-related assessments at Week 24 and Week 48, adverse-event outcomes, and changes in fasting lipid levels through Week 48. These outcomes cover virologic response, resistance, safety, and laboratory measures. Numerical findings are posted for the Week 48 suppression outcome, but numerical results for several other listed outcomes are not reported in the registry record.

The record does not report the trial's original sample-size justification, the intended analysis plan in enough detail to assess it, or whether interim analyses were planned or conducted. It also does not provide a detailed account of allocation procedures, adherence, or participant flow. Those omissions limit assessment of how the planned design was implemented and how the endpoint analysis population arose.

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: Of 132 patients enrolled, 109 were randomized to receive treatment, and 23 patients were not randomized for the following reasons: 10 did not meet study criteria; 5 withdrew consent; 3 were lost to follow-up, and 5 withdrew for other reasons.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All patients who received study drug and who had an HIV-1 RNA measurement at the analysis week.

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: All participants who received study drug

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With HIV-1 RNA Level <40 c/mL at Week 24, measured over From Day 1 to Week 24.

The primary endpoint is the percentage of participants with HIV-1 RNA below 40 c/mL at Week 24, measured from Day 1 through Week 24. The assay named in the registry is the Abbott m2000rt polymerase chain reaction assay. The outcome reduces each participant's Week 24 status to a responder or failure under the endpoint rules, then reports the proportion classified as responders in each arm.

The registry's response algorithm counts randomized patients who meet the response criteria in the numerator and describes all randomized patients as the denominator. Patients not meeting treatment-failure criteria are considered responders. Treatment failure includes discontinuation of study therapy or virologic rebound at or before Week 24; participants with treatment failure or a missing Week 24 HIV-1 RNA value are counted as failures. Rebound is defined as two consecutive on-treatment HIV-1 RNA levels at or above 40 c/mL, or a last on-treatment level at or above 40 c/mL followed by discontinuation.

This endpoint is useful for representing maintenance of virologic suppression while incorporating treatment failure and missing Week 24 measurements into the outcome rather than excluding them from the response definition. It is a binary response measure, so it does not describe the full distribution of RNA values among participants. The registry also gives a population description limited to patients who received study drug and had an HIV-1 RNA measurement at the analysis week. How that description relates to the stated all-randomized denominator is not reported in the registry record.

7. Results Posted in the Registry

• Atazanavir/Ritonavir + Tenofovir/Emtricitabine: 94.6% (35/37) versus 80.6% (58/72) on control; risk difference 14.0 percentage points (95% CI 2.3 to 25.7), risk ratio 1.17 (1.02–1.35); unadjusted two-proportion z-test p = 0.050.

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 With HIV-1 RNA Level <40 c/mL at Week 48

• 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:
  • Atazanavir/Ritonavir + Tenofovir/Emtricitabine: 86.5% (32/37) versus 69.4% (50/72) on control; risk difference 17.0 percentage points (95% CI 1.7 to 32.4), risk ratio 1.25 (1.02–1.52); unadjusted two-proportion z-test p = 0.051.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atazanavir/Ritonavir + Tenofovir/Emtricitabine and the control. The interval gives the range of effects that remain compatible with the data.

The posted Week 48 suppression proportions follow the same numerical direction as the primary Week 24 result, with a higher response percentage in the reference arm. This consistency in direction is relevant as a descriptive pattern, but the later outcome is secondary and its unadjusted comparison is close to the conventional threshold. It does not by itself establish a durable difference or resolve the uncertainty in the primary estimate.

The registry also lists outcomes concerning virologic rebound, resistance-related findings, adverse events, and fasting lipid changes. These outcomes address different aspects of treatment response and safety, rather than repeating the primary binary suppression measure. The record does not report numerical results for the listed rebound, resistance, and lipid outcomes. They cannot be used to infer a broader pattern of benefit or harm from the posted suppression percentages.

Unadjusted secondary results generally carry less inferential weight when multiple outcomes are examined and no multiplicity strategy is reported. In general, the more outcomes and comparisons considered, the greater the chance that at least one appears notable by chance. The record does not report a testing hierarchy, familywise error strategy, or other adjustment that would clarify how secondary comparisons were to be interpreted. The posted Week 48 p-value is therefore best read as an unadjusted result, alongside its estimate and confidence interval, rather than as independent confirmation of the primary finding.

Secondary outcomes can still add useful descriptive context, especially when they address different outcome domains or follow participants for longer. Their evidential contribution depends on how they were specified, measured, analyzed, and reported. Those details are not fully available in the registry record. The broad pattern should thus be limited to the posted suppression results, with no extrapolation to unreported outcomes.

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

• Percentage of Participants With HIV-1 RNA Level <40 c/mL at Week 48
• Number of Participants With Virologic Rebound at Weeks 24 and 48
• Number of Participants With Genotypable/Phenotypable Isolates, Emergent Genotypic Substitutions in Patients With Genotypable Isolates, and Phenotypic Resistance in Patients With Phenotypable Isolates at Week 24
• Number of Participants With Genotypable/Phenotypable Isolates, Emergent Genotypic Substitutions in Patients With Genotypable Isolates, and Phenotypic Resistance in Patients With Phenotypable Isolates at Week 48
• Number of Patients With Death as Outcome, Serious Adverse Events (SAEs), Treatment-related SAEs, Treatment-emergent Adverse Events (AEs) Leading to Discontinuation, and Treatment-emergent AEs
• Mean Changes in Fasting Lipid Levels From Baseline to Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary percentage: each participant is classified as a responder or not, and the arm-level result is the proportion classified as responders. The registry reports response percentages and 95% confidence intervals for each arm, together with an unadjusted comparison between the reference arm and the raltegravir arm. It reports the comparison as a risk difference. No adjusted primary analysis is reported in the registry record.

What does a risk difference describe?

In general, a risk difference is the difference between two proportions. It expresses the contrast on the probability scale, so a value of zero represents equal proportions and a positive value means the first proportion in the stated comparison is larger. For the Week 24 comparison, the registry gives a risk difference of 0.140 for the reference regimen relative to the raltegravir regimen. Its 95% confidence interval is 0.024 to 0.257. This contrast is distinct from a ratio measure, which describes relative rather than absolute separation between proportions.

The record also gives relative risk and odds ratio estimates. In general, a relative risk compares the two response probabilities as a ratio, while an odds ratio compares the odds of response. Ratios can be useful for describing relative association, but their values are not on the same scale as a risk difference. They can also appear quite different in magnitude from an absolute contrast. These are alternate descriptions of the same binary outcome, not separate trial outcomes. The registry's main comparison is reported as a risk difference.

What does a confidence interval add?

In general, a confidence interval describes the range of values compatible with the observed data under the method's assumptions. It conveys uncertainty around an estimate; it is not a guarantee that the true value lies within the particular interval, nor does it describe the spread of individual participant outcomes. The arm-level intervals and the interval for the difference address different quantities: one describes each arm's response proportion, while the other describes the contrast between arms.

For the Week 24 risk difference, the interval extends from 0.024 to 0.257. That range shows that the point estimate should not be read as an exact or highly precise value. The Week 48 interval for the difference, from 0.017 to 0.324, is also broad. Confidence intervals can include values that represent meaningfully different effect sizes, so interpretation should attend to the full range rather than only the central estimate.

How should the p-values be understood?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The registry reports unadjusted p-values of 0.05 for the Week 24 comparison and 0.051 for the Week 48 comparison. These values summarize the posted unadjusted tests, but the registry record does not report a multiplicity adjustment or a complete statistical analysis plan. They should not be interpreted in isolation from the estimates, confidence intervals, outcome hierarchy, and analysis limitations.

Unadjusted means the comparison is reported without an adjustment for the number of outcomes or comparisons being considered. In general, carrying out multiple tests creates more opportunities for a small p-value to arise by chance, even if no underlying differences exist. The registry lists several secondary outcomes, but the record does not state how the investigators intended to handle multiplicity. Consequently, the unadjusted secondary comparisons, where available, would ordinarily be treated as less conclusive than a prespecified primary analysis with a documented multiplicity strategy.

Why can binary-outcome analyses be sensitive to the data?

In general, a binary proportion depends on both the number of participants in the denominator and how many meet the response definition. With limited denominators, moving a small number of classifications can affect the estimated proportion and its uncertainty. These results are also affected by the outcome definition: here, treatment failure and missing Week 24 RNA measurements are classified as failures. The registry does not provide a component-by-component breakdown that would show how much each rule contributed to the totals.

Randomized assignment is intended to make groups comparable, on average, at the start of a study. It does not eliminate uncertainty in a particular trial, and it does not address every issue arising after assignment, such as missing measurements or discontinuation. In general, an intention-to-treat approach preserves participants in their randomized groups, while other populations may exclude some randomized participants. The response algorithm describes all randomized patients as the denominator, but the endpoint population statement refers to patients who received study drug and had an RNA measurement. The record does not clarify which definition governs the posted arm results.

The study was open-label. In general, lack of masking can influence behavior, treatment decisions, discontinuation, or assessment, although a laboratory measurement is less subjective than many clinical assessments. The registry identifies an RNA assay but does not describe blinding of laboratory personnel or other steps to reduce potential assessment bias. No claims about such procedures can be made from the registry record.

The posted calculations are unadjusted comparisons of response proportions. The registry does not report covariate-adjusted results, a detailed model specification, a missing-data sensitivity analysis, or an interim-analysis plan. These aspects therefore cannot be evaluated from the record. Statistical interpretation should remain tied to the estimates and definitions that are actually posted.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate less statistical uncertainty around an estimate, while wider intervals leave more possible values compatible with the data. At Week 24, the arm-level interval for atazanavir/ritonavir plus raltegravir is 69.5% to 88.9%, and the interval for atazanavir/ritonavir plus tenofovir/emtricitabine is 81.8% to 99.3%. The risk-difference interval is 0.024 to 0.257. Those ranges allow for a range of plausible response proportions and between-arm contrasts.

The Week 48 arm-level intervals are 57.5% to 79.8% and 71.2% to 95.5%, respectively. The risk-difference interval is 0.017 to 0.324. The intervals do not identify a single precise contrast; they leave uncertainty about how large the difference may be. The reported point estimates are the centers of the evidence summaries, not exact descriptions of the underlying response probabilities.

In general, interval width depends on the amount of information, the observed proportions, and the statistical method. The Week 24 arm denominators are 72 and 37, and the Week 48 denominators are also 72 and 37. The registry does not explain why these endpoint denominators are below the overall enrollment of 132. Differences between the endpoint population description and the response algorithm's denominator add uncertainty about exactly who is represented by the reported percentages.

Confidence intervals and p-values answer related but different questions. The interval shows a range of effect estimates compatible with the data and method, while the p-value summarizes evidence against a particular null value under its assumptions. A p-value near 0.05 does not make an estimate precise. The intervals and the modest denominators are important for judging how much the posted results can distinguish among possible effect sizes.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design justification. 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 set to a stated fraction of the observed effect. These calculations are participants per arm, not totals across both arms. The trial's own original design assumptions are not reported in the registry record.

For each planning scenario, the 80% power column gives the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were real and the assumptions held. The 90% power column gives the corresponding number per arm for a 90% chance. Higher target power generally requires a larger planned sample under otherwise identical assumptions.

The rows that use 100%, 75%, and 50% of the observed effect illustrate how the estimated planning requirement changes when the effect to detect is made smaller. Smaller effects are harder to distinguish from random variation, so they require more participants. The figures are not observations from this trial and are not evidence about the probability that its results are correct. This is not observed power; it is a forward-looking planning illustration using the stated assumptions and the observed effect as its starting point.

The planning figures should be read as conditional examples rather than as a reconstruction of the study's actual design. The registry does not report the trial's original sample-size calculation or its assumptions. The displayed planning assumptions also do not account for any design features or analysis choices beyond those explicitly stated, so the figures cannot establish whether the completed study was adequately sized for its original objective.

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 = 0.806; treatment proportion p₁ = 0.946; average p̄ = 0.876.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4665 = 0.9143.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4558 = 0.3836.
4. n = (0.9143 + 0.3836)² / (0.1404)² = 85.5, rounded up to 86 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 <- 0.805555555555556                          # control proportion
p1 <- 0.945945945945946                          # 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(1332227)
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 = 86 (80% power), 114 (90% power)
 75% of observed effect: n per arm = 172 (80% power), 229 (90% power)
 50% of observed effect: n per arm = 426 (80% power), 570 (90% power)
power.prop.test: 85.5 
Simulated power at n = 86 per arm: 0.826 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, but does not report a detailed statistical analysis plan, a testing hierarchy, or a multiplicity adjustment. The posted comparisons are described by unadjusted p-values. When multiple hypotheses are tested, the chance of at least one apparently unusual result can increase. In general, multiplicity procedures are used to control or describe that issue; without a reported procedure, secondary comparisons should be interpreted cautiously and the primary endpoint should remain the main inferential focus.

The record does not report whether interim analyses were planned or performed, whether stopping rules were used, or whether any adjustments were made for repeated looks at the data. The trial's original sample-size justification and its planned type I error strategy are also not reported in the registry record. These omissions prevent assessment of whether the posted analyses match a prespecified plan.

The response definition counts treatment failure or a missing Week 24 HIV-1 RNA result as failure. It defines rebound and describes discontinuation as one treatment-failure criterion. This rule is important because it determines how missing endpoint measurements enter the binary outcome. However, the endpoint population description says that patients received study drug and had an HIV-1 RNA measurement at the analysis week, while the algorithm says the denominator is all randomized patients. The registry record does not resolve this apparent difference or explain how missing data were handled in producing the arm denominators.

The available description does not include a missing-data sensitivity analysis, a comparison of included and excluded participants, or detailed participant-flow information. Nor does it report whether the main result was repeated in alternative analysis populations. Randomization is valuable, but post-randomization exclusions or missing measurements can complicate comparisons if the groups are no longer represented in the same way. The population ambiguity matters for that reason.

The record identifies the study as open-label and randomized but does not provide enough detail to evaluate allocation concealment, masking of outcome assessors, covariate adjustment, or other protections against bias. It is not reported in the registry record whether any of these procedures were used. These gaps do not change the posted values, but they limit assessment of how robustly the analyses address multiplicity, missingness, and potential bias.

15. 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: accidental overdose (2.7%), cachexia (1.4%), device related infection (1.4%), gastrooesophageal reflux disease (1.4%), calculus urinary (1.4%).

The serious adverse event counts are 4 among 72 participants in the atazanavir/ritonavir plus raltegravir group and 1 among 37 participants in the atazanavir/ritonavir plus tenofovir/emtricitabine group. These are counts within the registry's serious-event reporting categories; they are not, by themselves, estimates of a causal treatment effect. The record also reports other adverse events for 27 of 72 and 23 of 37 participants, respectively. Serious and other adverse-event counts represent distinct reporting categories and should not be combined.

The listed serious-event terms include accidental overdose at 2.7%, and cachexia, device related infection, gastrooesophageal reflux disease, calculus urinary, and non-cardiac chest pain at 1.4% each. The registry's summary does not provide enough context to assign these terms to a particular arm or to determine causal relationship from the percentages alone. Death counts are not reported in the registry record.

Adverse-event counts are descriptive. Interpretation depends on event definitions, follow-up, exposure, severity, and attribution, and the record does not provide a complete account of those details. The counts should therefore be read as the events posted for each group, not as proof that one regimen caused more or fewer events.

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

The posted data show that a larger percentage of participants in the atazanavir/ritonavir plus tenofovir/emtricitabine group met the registry's Week 24 response definition than in the atazanavir/ritonavir plus raltegravir group. The Week 48 response proportions have the same numerical ordering. The risk-difference estimates and their confidence intervals describe uncertainty around those contrasts. The Week 24 unadjusted p-value is 0.05, and the Week 48 unadjusted p-value is 0.051; neither value removes the need to consider interval width, multiplicity, or population definition.

These results do not show that the observed arm difference is exactly the estimated difference in the broader population, nor do they establish why the proportions differ. The endpoint definition includes treatment failure and missing measurements, and the record does not provide a detailed breakdown of those components. The endpoint's population statement and its all-randomized denominator wording are not fully aligned in the registry record. That uncertainty makes it important not to overstate who the posted proportions represent.

The study addresses a specific switch question in virologically suppressed people with HIV-1 who were experiencing safety and/or tolerability issues on their prior regimen. It does not directly answer questions about people outside that described population, other regimens, or outcomes not reported in the record. The registry describes a phase 4 randomized open-label study, but the posted results alone do not establish a treatment recommendation or provide a complete comparison of safety and efficacy.

The listed secondary outcomes cover rebound, resistance, adverse events, and lipid changes, but numerical results for several of these outcomes are not reported in the registry record. The absence of those results prevents a comprehensive interpretation across all planned outcome domains. Likewise, the record does not report the original sample-size justification, interim analyses, or a full statistical plan. Conclusions should remain proportionate to the posted outcomes and the uncertainty around them.

In general, a trial result is one contribution to an evidence base rather than a stand-alone decision rule. The randomized comparison is informative about the assigned groups as studied, while missing methodological details and unreported outcomes limit the strength and scope of conclusions that can be drawn from this record.

17. Why This Trial Matters Statistically

This trial illustrates why a response percentage and its uncertainty should be read together. The Week 24 point estimates differ in direction and size from what would be conveyed by either arm percentage alone, while the confidence interval for the risk difference shows a range of plausible contrasts. A p-value at the conventional threshold does not make that estimate precise or resolve the practical importance of the difference.

It also highlights how endpoint definitions shape analysis. Counting missing Week 24 measurements and treatment failures as failures makes those events part of the response outcome. That can be a transparent way to define a treatment-response measure, but the population wording must still be clear. Here, the registry's description of an all-randomized denominator sits alongside a population statement limited to participants who received study drug and had an RNA measurement. Resolving that distinction is important for judging what the arm percentages represent.

The study further demonstrates the need to distinguish a prespecified primary comparison from secondary findings. The Week 48 result follows the same numerical direction, but is an unadjusted secondary comparison, and the registry does not report a multiplicity strategy. Other listed outcome domains lack numerical results in the record. A pattern across posted outcomes should not be mistaken for a complete account of the study.

Finally, planning calculations based on an observed effect are not evidence of the trial's original design rationale or of its probability of success. The record's lack of a sample-size justification and detailed statistical plan limits retrospective evaluation of design choices. These are general statistical lessons grounded in the trial's posted response comparisons and documentation gaps.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The most immediate limitation is uncertainty about the endpoint analysis population. The primary endpoint description identifies patients who received study drug and had an RNA measurement at the analysis week, while the response algorithm describes all randomized patients as the denominator. The registry record does not say which wording governs the posted results or explain why the endpoint denominators are 72 and 37 when overall enrollment is 132.

The study was open-label, and the registry does not report whether outcome assessment or laboratory analysis was masked. HIV-1 RNA is an assay-based outcome, but the response algorithm also incorporates discontinuation and missing measurement status. Knowledge of assigned regimen could potentially relate to treatment decisions or discontinuation; the record does not provide information to evaluate that possibility.

The posted response results do not include a component breakdown showing how many failures arose from rebound, discontinuation, or missing Week 24 measurements. The record also does not report detailed participant flow, adherence, or baseline characteristics that could help assess the comparability of participants contributing to the endpoint analysis. No sensitivity analyses for missing data or alternative analysis populations are reported.

The Week 48 suppression comparison is secondary, and the registry does not describe multiplicity control. Numerical findings are not reported for several other listed outcomes, including rebound, resistance, and lipid changes. Safety counts are available, but the record does not fully describe exposure time, causal attribution, or the context for each event term. Death counts are not reported in the registry record.

Finally, the original sample-size justification, detailed statistical analysis plan, and any interim-analysis procedures are not reported in the registry record. These limitations do not invalidate the posted values, but they constrain assessment of robustness, generalizability, and the intended inferential framework.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Atazanavir/Ritonavir, Once Daily + Raltegravir, Twice Daily, Switch Study in HIV-1-Infected Patients — NCT01332227.
• Registry record last updated 2015-02-19; status last verified 2015-02.
• Results first posted 2014-10-16.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01332227 was a completed phase 4 randomized, open-label, parallel-group switch study sponsored by Bristol-Myers Squibb. It enrolled 132 participants with HIV-1 who were described as virologically suppressed but experiencing safety and/or tolerability issues on their current regimen. The study compared atazanavir/ritonavir plus raltegravir with atazanavir/ritonavir plus tenofovir/emtricitabine.

The primary outcome was the percentage with HIV-1 RNA below 40 c/mL at Week 24. The posted response percentages were 80.6% and 94.6%, respectively, with an unadjusted risk difference of 0.140 and a 95% confidence interval from 0.024 to 0.257. The Week 48 response percentages followed the same numerical direction. Interpretation is limited by uncertainty in the endpoint population wording, unadjusted secondary testing, and missing results for several listed outcomes.