A Trial of 2 Options for Second Line Combination Antiretroviral Therapy Following Virological Failure of a Standard Non-nucleoside Reverse Transcriptase Inhibitor (NNRTI)+2N(t)RTI First Line Regimen: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial of 2 Options for Second Line Combination Antiretroviral Therapy Following Virological Failure of a Standard Non-nucleoside Reverse Transcriptase Inhibitor (NNRTI)+2N(t)RTI First Line Regimen (NCT00931463), a randomized phase 4 study. The primary outcome is Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization.

2. Clinical Question

The clinical question is a comparison of two active combination regimens in a second-line treatment setting after virological failure, not a comparison with no treatment. The endpoint focuses on virological suppression at a specified follow-up time. It does not by itself cover the other outcomes named in the registry record, including immunological, safety, clinical, metabolic, adherence, resistance, or quality-of-life outcomes.

The posted primary results report suppression counts for each randomized arm and a risk difference comparing raltegravir with 2N(t)RTI. Those results describe the observed endpoint in the stated analysis population. They do not establish that the regimens are equivalent: interpreting comparability requires attention to the uncertainty around the estimated difference and to whether a non-inferiority or equivalence margin was specified. Such a margin is not reported in the registry record.

3. Trial Design

This was a phase 4, randomized, open-label, parallel-group study. The registry record lists an enrollment of 558. Participants were assigned to ritonavir-boosted lopinavir with 2N(t)RTI or ritonavir-boosted lopinavir with raltegravir. Masking is listed as none, so the trial was open-label rather than blinded.

The study was planned to run for 96 weeks, with the primary endpoint analyzed after 48 weeks. The primary completion date is listed as 2012-09, and the trial status is completed. The registry record lists the start as 2009-09 and the sponsor as the Kirby Institute. The primary outcome compares the number of participants with plasma HIV RNA < 200 copies/mL at 48 weeks after randomization.

The primary result is labeled modified intention-to-treat. The registry record does not describe the exact rules used to define this population, such as how post-randomization exclusions or missing endpoint values were handled. Four secondary outcome descriptions are posted, including per-protocol analyses, a per-protocol analysis classifying non-completers as failures, and per-protocol analyses by baseline viral-load category. The posted results do not include reported analyses for those outcomes.

The registry record identifies the allocation as randomized but does not report the sequence-generation method, allocation concealment, or details of how assignment was implemented. It also does not report the original sample-size justification, the target difference used in planning, or a statistical analysis plan. These details matter when judging how closely the posted outcome analyses follow the trial's original design and how the study was intended to assess the hypothesis of comparable efficacy.

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: 558 participants were enrolled in the study. 14 were excluded because of unverifiable data at one site and 3 dropped out before analysis, never received study treatment

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: modified intention-to-treat

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 Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, measured over 48 weeks following randomization.

The primary endpoint counts participants whose plasma HIV RNA was below 200 copies/mL 48 weeks after randomization. It is a binary outcome at the participant level: each participant either meets the stated suppression threshold at the specified time or does not. The registry record reports counts in the modified intention-to-treat population, with 219 of 271 in the lopinavir and 2N(t)RTI arm and 223 of 270 in the lopinavir and raltegravir arm.

A threshold-based virological endpoint gives a clinically interpretable way to compare whether participants achieved suppression at a fixed follow-up point. It reduces a laboratory measurement to a yes-or-no outcome, which can be summarized as a proportion in each arm and contrasted using a risk difference. That convenience comes with a limitation: it does not show how far above or below the threshold individual viral-load values were, or how suppression changed over time. Those details are not included in the primary result.

The endpoint is used as the primary outcome because the study question concerns virological suppression after second-line therapy. The registry record also names other outcome domains, but the primary endpoint alone cannot summarize safety, resistance, adherence, quality of life, or longer-term clinical outcomes. The 48-week result is therefore evidence about the specified virological measure at that time, rather than a complete account of every potential benefit or harm.

7. Results Posted in the Registry

• Ritonavir-boosted Lopinavir and Raltegravir: 82.6% (223/270) versus 80.8% (219/271) on control; risk difference 1.8 percentage points (95% CI -4.7 to 8.3), risk ratio 1.02 (0.94–1.11); unadjusted two-proportion z-test p = 0.592.

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.

Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ritonavir-boosted Lopinavir and Raltegravir: 85.8% (211/246) versus 84.7% (211/249) on control; risk difference 1.0 percentage points (95% CI -5.2 to 7.3), risk ratio 1.01 (0.94–1.09); unadjusted two-proportion z-test p = 0.746.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ritonavir-boosted Lopinavir and Raltegravir and the control. The interval gives the range of effects that remain compatible with the data.

Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population, Non-completer Classed as Failure

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ritonavir-boosted Lopinavir and Raltegravir: 77.8% (210/270) versus 76.8% (208/271) on control; risk difference 1.0 percentage points (95% CI -6.0 to 8.1), risk ratio 1.01 (0.92–1.11); unadjusted two-proportion z-test p = 0.776.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ritonavir-boosted Lopinavir and Raltegravir and the control. The interval gives the range of effects that remain compatible with the data.

Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population, Baseline VL >100,000 Copies Per mL

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ritonavir-boosted Lopinavir and Raltegravir: 65.0% (39/60) versus 59.6% (31/52) on control; risk difference 5.4 percentage points (95% CI -12.6 to 23.4), risk ratio 1.09 (0.82–1.46); unadjusted two-proportion z-test p = 0.557.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ritonavir-boosted Lopinavir and Raltegravir and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes examine the same 48-week virological threshold through different analysis populations and baseline viral-load categories. Taken together, their recalculated point estimates are positive, in the direction of a higher suppression proportion with lopinavir and raltegravir. Each reported interval includes zero, so none of these alternate comparisons sharply distinguishes a difference from no difference. This broad pattern is consistent with the primary result's uncertain, modest positive point estimate rather than presenting a clear reversal.

The secondary analyses are related to, but do not replace, the primary analysis. A per-protocol population asks how results look among participants included under protocol-based criteria, while the non-completer-as-failure version imposes a particular approach to participants who did not complete follow-up. The baseline viral-load analyses ask whether results look different within listed categories, but separate subgroup estimates do not by themselves show that treatment effects differ between categories. Such a claim would require an interaction assessment, which is not reported in the registry record.

These secondary results should carry less weight than the primary outcome because they are additional analyses, involve altered populations or subgroup definitions, and are not accompanied by reported sponsor analyses. Multiple looks at outcomes or subgroups increase the chance that some estimates appear notable by chance. The registry record does not report a multiplicity plan or adjusted secondary inferential results. The posted unadjusted values therefore should be interpreted as exploratory or supportive descriptions, rather than as independent confirmation of a treatment difference.

The registry record lists four secondary outcome descriptions and no reported analyses for them. The counts and recalculated comparisons make it possible to describe the pattern, but they do not reveal whether these analyses were prespecified, how missing values were handled across all versions, or whether any were designated as confirmatory. The secondary endpoints can add context about sensitivity to analysis choices, but the lack of those details means they cannot settle the primary uncertainty or establish comparability on their own.

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

• Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population
• Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population, Non-completer Classed as Failure
• Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population, Baseline VL >100,000 Copies Per mL
• Participants With Plasma HIV RNA < 200 Copies/mL 48 Weeks After Randomization, Per-protocol Population, VL Less Than or Equal to 100,000 Copies Per mL

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the other. For this trial, the comparison is oriented as ritonavir-boosted lopinavir and raltegravir relative to ritonavir-boosted lopinavir and 2N(t)RTI. A positive estimate means the event proportion is higher in the raltegravir arm; a negative estimate means it is lower. Here, the event is meeting the endpoint of plasma HIV RNA < 200 copies/mL. The primary risk difference is 0.018. It is a contrast between the observed proportions, not a statement about each participant's individual response.

Risk differences are expressed on the absolute probability scale. They can be easier to interpret as a direct comparison of event proportions than a relative measure, but their meaning still depends on the endpoint, analysis population, and follow-up time. A risk difference at 48 weeks does not describe when suppression occurred or whether it was sustained throughout follow-up.

What does an interval around an estimate add?

A confidence interval represents uncertainty in an estimated effect under the assumptions of the method used to calculate it. It gives a range of values reasonably compatible with the observed data and that method. It is not a guarantee that the true effect lies in the interval, and it does not express the probability that one treatment is better. The primary reported interval runs from -0.047 to 0.083. Because it includes zero, the results do not distinguish a zero risk difference from effects in either direction at the interval's stated level. The confidence level for the posted intervals is not reported in the registry record.

Intervals are generally more informative than a p-value alone because they show both the direction and scale of effects that remain plausible under the analysis. An interval can include zero while still allowing effects that may matter clinically. Deciding what range is clinically important requires context and, for a non-inferiority or equivalence question, a prespecified margin. The registry record does not report such a margin.

What is the role of a p-value?

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary unadjusted p-value is 0.592. That value does not establish sameness; it indicates that the observed contrast is not statistically distinguishable from zero by this unadjusted test. The registry record does not report a sponsor analysis or a complete inferential plan, so the recalculated p-value should not be treated as a substitute for the trial's prespecified analysis.

Why distinguish analysis populations?

The primary result is labeled modified intention-to-treat, while the posted secondary results use per-protocol populations or alternate endpoint handling. An intention-to-treat approach is generally intended to preserve the benefits of random assignment by analyzing participants according to their randomized groups. A modified version may apply exclusions or other rules; the specific definition is not reported in the registry record. A per-protocol analysis generally focuses on participants meeting protocol-defined conditions, but the conditions and exclusions used in this trial are not described in the registry record.

Different analysis populations can produce different denominators and estimates because they include different sets of participants or handle endpoint availability differently. Such analyses can help assess robustness, but they can also lose some protection against bias associated with randomization. In this trial, one secondary endpoint explicitly classifies non-completers as failures. That is a different missing-outcome assumption from simply analyzing observed outcomes, and it is informative as a sensitivity approach only if interpreted as such. The exact handling of other missing data is not reported.

Why do these recalculations have limits?

The posted risk differences, intervals, relative measures, and unadjusted p-values are simple unadjusted recalculations from the registry's summary statistics. They do not adjust for baseline characteristics, account for any design features beyond the posted information, or use individual participant data. The registry record does not report adjusted analyses, the confidence-interval method, or the statistical model used for a sponsor analysis. Since no reported analyses are listed, the recalculations are a transparent descriptive aid rather than a replacement for the trial's own prespecified methods.

Binary outcomes count participants meeting a definition, rather than measuring a continuous distribution. This makes interpretation depend on the threshold and on how participants without a measured endpoint are treated. The primary threshold is stated, but the modified intention-to-treat rules are not. The secondary results offer some alternate population and missing-outcome definitions, yet do not resolve every uncertainty about endpoint ascertainment or analysis choices. Those methodological limits should be kept in view when comparing estimates or drawing conclusions from the trial.

11. Confidence Intervals and Precision

The primary risk difference is 0.018, with a reported interval from -0.047 to 0.083. Its span across zero indicates that the observed data do not pin down the direction of the difference. The interval allows values favoring either arm, as well as values close to no difference. The arm proportions, 0.808 for lopinavir and 2N(t)RTI and 0.826 for lopinavir and raltegravir, are close as point estimates, but point estimates alone do not convey how uncertain the comparison is.

The interval is the main guide to precision: a range extending in both directions should not be read as evidence that the regimens have identical effects. Nor does the interval establish that any particular effect within its bounds is clinically important. Clinical interpretation would require a judgment about what difference matters, and an equivalence or non-inferiority assessment would require a suitable prespecified margin. Neither is reported in the registry record. The confidence level and calculation method for the posted interval are also not reported in the registry record.

The secondary intervals likewise include zero, with some extending across a broad range of possible differences. The per-protocol subgroup defined by baseline viral load has less information than the overall primary analysis, reflected in a notably broad interval, so its estimate is especially uncertain. These secondary estimates should not be used to claim a subgroup-specific effect without a prespecified interaction analysis, which is not reported in the registry record.

Precision is distinct from statistical significance and from clinical importance. A narrow interval would indicate more precise estimation, while a broad interval leaves more uncertainty. The primary result provides an estimate in the positive direction but does not tightly determine the true difference or rule out effects in the other direction. The registry record's absence of sponsor-reported analyses and details of the interval method further limits what can be inferred about the precision calculation.

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 illustration is based on the primary observed effect and gives participants per arm, not a total across arms or a count of events. Its 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 the stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 7,400 participants per arm for 80% power and 9,905 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 13,279 participants per arm for 80% power and 17,776 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 30,155 participants per arm for 80% power and 40,369 participants per arm for 90% power.

In plain terms, the 80% power column describes a planning target intended to give the specified test an 80% chance of detecting the assumed effect if that effect were the true one and the stated assumptions held. The 90% column uses a higher detection probability under the same kind of planning assumptions. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. The curve represents this general relationship between the assumed effect size and the number of participants needed.

These figures are planning illustrations, not observed power. They are derived from the observed effect for illustration and do not establish the rationale used when the trial was originally designed. In particular, they should not be used to conclude that the completed trial was adequately or inadequately powered without the original target effect, planned analysis, and design assumptions.

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 = 0.808; treatment proportion p₁ = 0.826; average p̄ = 0.817.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5468 = 1.0717.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5467 = 0.4601.
4. n = (1.0717 + 0.4601)² / (0.0178)² = 7,399.1, rounded up to 7,400 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 <- 0.808118081180812                          # control proportion
p1 <- 0.825925925925926                          # 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(931463)
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 = 7,400 (80% power), 9,905 (90% power)
 75% of observed effect: n per arm = 13,279 (80% power), 17,776 (90% power)
 50% of observed effect: n per arm = 30,155 (80% power), 40,369 (90% power)
power.prop.test: 7399.1 
Simulated power at n = 7,400 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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy for the primary and secondary outcomes, a hierarchy of hypotheses, or a plan for controlling the chance of false-positive findings across multiple tests. Without such information, unadjusted secondary p-values should be treated cautiously. When many outcomes, populations, or subgroups are examined, the chance of at least one apparently notable result can increase even if there is no real effect. That general concern applies to interpreting a collection of secondary analyses, but the registry record does not establish how many were planned beyond the listed outcome descriptions.

The record lists no reported analyses. It therefore does not provide sponsor-reported model results, adjusted estimates, multiplicity-adjusted p-values, or a complete statistical analysis plan. The comparison statistics discussed for the posted outcomes are recalculated, unadjusted summaries. Whether they correspond to the original prespecified analysis is not reported in the registry record.

Missing-data handling is only partly visible from the outcome descriptions. The primary result is labeled modified intention-to-treat, but the exact definition and handling of participants without an available 48-week measurement are not reported. One secondary outcome explicitly classifies non-completers as failures. This is a meaningful sensitivity definition, but the registry record does not state how other missing observations were treated, whether missingness was common for particular reasons, or whether additional approaches were used.

The primary modified intention-to-treat and secondary per-protocol populations answer related but not identical questions. Modified intention-to-treat analyses can exclude some randomized participants depending on their definition; per-protocol analyses can also depart from the original randomized groups. The registry record does not report the rules behind these populations, so the potential impact of exclusions cannot be fully assessed. The posted denominators show which counts were used in each summary, but do not explain why participants were or were not included.

Interim analyses, stopping rules, sequence generation, allocation concealment, and the original sample-size justification are not reported in the registry record. Their absence does not show that these procedures were absent from the trial; it means their details cannot be evaluated from this record. Together, these missing analysis and design details limit assessment of prespecification, missing-data bias, and the strength of inferences from the secondary results.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pregnancy (2.6%), pneumonia (1.1%), acute gastroenteritis (0.7%), anaemia (0.7%), pulmonary tuberculosis (0.7%).

The registry record reports serious adverse events in 23 of 271 participants receiving ritonavir-boosted lopinavir and 2N(t)RTI, and in 24 of 270 receiving ritonavir-boosted lopinavir and raltegravir. These are counts of participants recorded with serious adverse events, not a complete description of event timing, duration, severity patterns, or causal attribution. The registry record does not report death counts in the adverse-event summary.

The serious-event terms listed include Pregnancy (2.6%), pneumonia (1.1%), Acute gastroenteritis (0.7%), Anaemia (0.7%), Pulmonary tuberculosis (0.7%), and Death, cause unknown (0.7%). These percentages are listed as serious-event terms; the registry record does not provide the term-specific denominators or arm-specific breakdowns alongside them. They should not be interpreted as direct comparative risks between the trial arms.

Serious adverse-event counts are useful for describing events recorded during the study, but they do not establish that a regimen caused an event or that the two regimens have the same safety profile. The record does not provide detailed comparative safety analyses, confidence intervals, event adjudication, or a full account of adverse events by severity and timing. These figures should be read as registry safety summaries, not as a complete causal assessment.

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

The posted primary result shows that suppression below the stated threshold was common in both randomized groups at 48 weeks. The observed proportions were 0.808 with ritonavir-boosted lopinavir and 2N(t)RTI and 0.826 with ritonavir-boosted lopinavir and raltegravir. The recalculated risk difference is 0.018 in the direction of the raltegravir arm, but the interval from -0.047 to 0.083 leaves uncertainty about both the direction and size of the difference.

This result does not prove that the regimens are equivalent, interchangeable, or equally effective. A non-significant unadjusted test is not an equivalence test, and the registry record does not report an equivalence or non-inferiority margin. The estimate also does not show that either regimen caused suppression in every participant, because the posted result is a group-level comparison and does not describe individual outcomes beyond the counts.

The result is limited to the specified endpoint, analysis population, and follow-up time. It does not establish longer-term durability, changes in viral load across the full study period, resistance outcomes, adherence, quality of life, metabolic effects, immunological outcomes, or clinical outcomes. Although the registry record lists these domains among secondary and exploratory endpoints, the posted results do not report their analyses. The serious adverse-event summary supplies counts and listed event terms, but not enough detail to establish causal safety differences between regimens.

A balanced reading is that the observed primary proportions are close, while the interval leaves meaningful uncertainty around the contrast. The trial's stated hypothesis was comparable efficacy, but a conclusion about comparability requires the intended margin and design-based analysis, neither of which is reported in the registry record. The available summaries can inform an understanding of the observed 48-week result, but they cannot answer every clinical or safety question about these regimens.

17. Why This Trial Matters Statistically

This trial illustrates why an observed difference, a significance test, and a claim of equivalence are distinct statistical ideas. The primary estimate favors the raltegravir arm numerically, but the reported interval crosses zero and the unadjusted p-value is 0.592. That combination does not establish a difference, yet it also does not demonstrate that the regimens perform identically. The distinction is central whenever a study question is framed around comparable efficacy.

The trial also shows how analysis populations affect interpretation. The primary summary uses a modified intention-to-treat population, while the secondary summaries include per-protocol analyses and an explicit non-completer-as-failure approach. These alternative views can test whether the broad pattern changes under different definitions, but their meaning depends on transparent population rules and missing-data assumptions. Those details are not reported in the registry record.

Finally, the posted planning illustration highlights the relationship between effect size and required sample size. When the assumed effect is reduced to a smaller fraction of the observed effect, the planning values increase. This helps explain why a small estimated difference can be difficult to assess precisely, but the illustration is not the trial's original design calculation and is not observed power. Together, the results provide a useful case for separating descriptive estimates from confirmatory claims and for asking whether registry reporting contains the design information needed to interpret each claim.

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.

The registry record does not provide an equivalence or non-inferiority margin, even though the study rationale describes comparable efficacy as the hypothesis. Without that margin and the original analysis plan, the primary result cannot establish whether the observed uncertainty meets a formal criterion for comparability. Sponsor-reported analyses are not listed, so the posted comparison rests on recalculated unadjusted summary statistics.

The definition of the modified intention-to-treat population is not reported. Nor are the reasons for missing endpoint data, the handling of missing values in the primary analysis, or the exact rules defining the per-protocol populations. The secondary analysis that classifies non-completers as failures offers one alternate approach, but does not resolve uncertainty about other missing-data assumptions or whether missingness differed by arm.

Further details relevant to evaluating conduct and analysis are not reported in the registry record, including allocation concealment, randomization implementation, the original sample-size justification, interim analyses, stopping rules, and a multiplicity plan. The confidence level and method used for the posted intervals are also not reported. These omissions limit assessment of prespecification and of how the posted summaries relate to the trial's intended analysis.

The endpoint is a thresholded measure at 48 weeks, so it does not show individual viral-load values, the timing or durability of suppression, or outcomes beyond that measurement. The secondary results are unadjusted and include subgroup analyses; they should not be treated as independent confirmation of an effect. Safety reporting is also summarized: serious-event counts and a list of terms do not provide detailed timing, attribution, or a full arm-specific account of each event. These limitations do not invalidate the posted counts, but they constrain the conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Trial of 2 Options for Second Line Combination Antiretroviral Therapy Following Virological Failure of a Standard Non-nucleoside Reverse Transcriptase Inhibitor (NNRTI)+2N(t)RTI First Line Regimen — NCT00931463.
• Registry record last updated 2026-03-27; status last verified 2019-08.
• Results first posted 2014-01-17.
• 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

NCT00931463 is a completed, phase 4, randomized, open-label, parallel-group study sponsored by the Kirby Institute. It compared ritonavir-boosted lopinavir with 2N(t)RTI against ritonavir-boosted lopinavir with raltegravir in participants virologically failing first-line NNRTI/2N(t)RTI therapy. The primary endpoint was plasma HIV RNA < 200 copies/mL at 48 weeks after randomization.

In the modified intention-to-treat result, the posted proportions were 0.808 and 0.826, and the recalculated unadjusted risk difference was 0.018, with an interval from -0.047 to 0.083. The interval includes zero, so the direction and size of the difference remain uncertain. The record does not report sponsor analyses, a statistical analysis plan, or a non-inferiority or equivalence margin; the findings therefore do not establish comparable efficacy. Secondary results offer alternate analysis views, while safety summaries report serious-event counts and selected event terms without detailed comparative analysis.