A Study to Compare Effectiveness and Safety of Darunavir/Ritonavir (DRV/Rtv) 800mg/100mg Once Daily Versus DRV/Rtv 600mg/100mg Twice Daily in Early Treatment-Experienced HIV-1 Infected Patients (ODIN): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare Effectiveness and Safety of Darunavir/Ritonavir (DRV/Rtv) 800mg/100mg Once Daily Versus DRV/Rtv 600mg/100mg Twice Daily in Early Treatment-Experienced HIV-1 Infected Patients (ODIN) (NCT00524368), a randomized phase 3 study. The primary outcome is Virological Response at Week 48 (Number of Participants With Plasma Viral Load Less Than 50 Copies/mL) - as Defined by the Time to Loss of Virologic Response (TLOVR) Algorithm.

2. Clinical Question

The question concerns a comparison of two dosing schedules for the same drug combination, rather than a comparison with no treatment or placebo. Both regimens were administered alongside selected optimized background therapy. Consequently, the randomized comparison concerns the regimens as studied in that treatment context; it does not isolate the contribution of darunavir/ritonavir from background therapy.

The registry describes the study as randomized, open-label, and parallel-group. Open-label means treatment assignment was not masked from participants or study personnel according to the registry. Randomization supports a treatment-group comparison, while lack of masking can matter for outcomes involving judgment, behavior, or reporting. The primary endpoint is a laboratory-based viral-load response, but the registry's response algorithm also includes rules for discontinuation, missing visits, and confirmed virologic failure.

3. Trial Design

The registry identifies this as a randomized, open-label, parallel-group Phase 3 trial of darunavir/ritonavir in early treatment-experienced HIV-1 participants. It records enrollment of 590 and a completed study. The two assigned strategies were 800/100 mg once daily and 600/100 mg twice daily, each used with selected optimized background regimen therapy. The arm descriptions specify the tablet and capsule schedules.

The primary outcome was assessed at Week 48: the number of participants meeting the viral-load threshold of less than 50 copies/mL under the TLOVR algorithm. The registry also lists secondary outcomes covering response at a less stringent viral-load threshold, viral-load change, timing of initial response and loss of response, CD4+ cell count, HIV-related functional assessment, and self-reported adherence. This range of outcomes includes laboratory measures, time-to-event measures, and participant-reported measures, which do not all answer the same question.

For the primary endpoint, the posted arm counts are 212 of 294 for once-daily treatment and 210 of 296 for twice-daily treatment. The primary population is described as intention to treat, with permanent discontinuations treated as nonresponses after discontinuation. The TLOVR rules also address intermittent missing viral-load values and confirmed failure. Those rules are important to interpreting the endpoint because the outcome is not simply a count of participants with an observed low viral load at one visit.

The registry record does not report the original sample-size justification, the original design assumptions, a detailed protocol for the optimized background regimen, or interim-analysis procedures. It also does not report the non-inferiority margin in the material describing the primary analysis. Those omissions prevent a full reconstruction of the design rationale or an independent assessment of whether the reported analysis met a prespecified margin.

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: In total 1092 participants were screened, of which 590 participants were randomly assigned and treated (294 participants were treated with DRV/rtv 800/100 mg once daily, and 296 participants with DRV/rtv 600/100 mg twice daily.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention To Treat (ITT) population: Participants who permanently discontinued were considered nonresponders after discontinuation. Participants with intermittent missing viral load values were considered responders if preceeding and succeeding visits indicated response. Otherwise, intermittent values were imputed with nonresponse.

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 Virological Response at Week 48 (Number of Participants With Plasma Viral Load Less Than 50 Copies/mL) - as Defined by the Time to Loss of Virologic Response (TLOVR) Algorithm, measured over 48 Weeks.

The primary endpoint is the number of participants with plasma viral load below 50 copies/mL at Week 48, classified using the time to loss of virologic response (TLOVR) algorithm. This is a binary outcome: each participant is classified as a responder or nonresponder under the algorithm's rules. It captures whether viral suppression below the threshold was achieved and maintained according to those rules, rather than merely recording a single viral-load measurement.

The registry specifies that response and loss of response had to be confirmed at two consecutive visits. Participants who permanently discontinued were considered nonresponders after discontinuation. Intermittent missing viral-load values were treated as response when both the preceding and succeeding visits indicated response; otherwise, the missing values were imputed as nonresponse. Resuppression after confirmed virologic failure counted as failure in this algorithm.

General statistical context: prespecified endpoint definitions help make the outcome reproducible and reduce ambiguity about how participant histories translate into a final response classification. A binary response endpoint is also straightforward to express as a proportion in each group and as a difference between proportions. However, the resulting comparison depends on the threshold, follow-up point, and missing-data and discontinuation rules. The endpoint therefore describes response under this particular algorithm and time point, not every aspect of viral control or treatment experience.

The registry's primary endpoint is clinically interpretable as a virological response measure, but the registry record does not report the rationale for choosing this threshold over other possible thresholds. Nor does the endpoint, by itself, establish differences in symptoms, quality of life, safety, or longer-term outcomes.

7. Results Posted in the Registry

• DRV/Rtv 600/100 mg Twice Daily: 70.9% (210/296) versus 72.1% (212/294) on control; risk difference -1.2 percentage points (95% CI -8.4 to 6.1), risk ratio 0.98 (0.89–1.09); unadjusted two-proportion z-test p = 0.754.

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.

Virologic Response at Week 48 (Viral Load Less Than 400 Copies/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:
  • DRV/Rtv 600/100 mg Twice Daily: 76.7% (227/296) versus 76.9% (226/294) on control; risk difference -0.2 percentage points (95% CI -7.0 to 6.6), risk ratio 1.00 (0.91–1.09); unadjusted two-proportion z-test p = 0.958.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DRV/Rtv 600/100 mg Twice Daily and the control. The interval gives the range of effects that remain compatible with the data.

Time to Reach First Virologic Response

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazards); it was not recalculated.
• Result:
  • DRV/Rtv 800/100 mg Once Daily vs DRV/Rtv 600/100 mg Twice Daily: hazard ratio 0.99 (95% CI 0.82–1.19), reported p = 0.917 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between DRV/Rtv 800/100 mg Once Daily vs DRV/Rtv 600/100 mg Twice Daily and the control. The interval gives the range of effects that remain compatible with the data.

Time to Loss of Virologic Response

• 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 errors.
• Result:
  • DRV/Rtv 600/100 mg Twice Daily: mean 281.74 versus 250.24 on control; difference 31.51 (95% CI 11.97 to 51.04), standardized effect d = 0.26; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for DRV/Rtv 600/100 mg Twice Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry's secondary outcomes span viral suppression under another threshold, viral-load change, time to initial response, time to loss of response, immune-cell change, HIV-related function, and adherence. The listed outcomes therefore extend beyond the primary response classification, but they use different scales and answer different questions. The pattern should not be compressed into a single claim that all outcomes agree or disagree.

Some outcomes are closely related to the primary endpoint because they also describe viral response, while others address response timing, immune status, function, or reported adherence. Agreement across related viral measures can offer context, but it does not turn them into independent confirmations: outcomes can be correlated because they arise from the same participants and related biological or measurement processes. Outcomes farther from the primary endpoint may provide additional dimensions, but they do not directly establish the primary response result.

The registry lists 11 secondary outcomes. The detailed numerical results and analyses are not reported in the registry record for every listed outcome in the statistical summary. The reported secondary analyses use different methods, including logistic regression and Cox regression, and the simple recalculations do not all estimate the same quantity as the sponsor analyses. Their values should therefore be interpreted endpoint by endpoint rather than ranked as if they were one common measure.

General statistical context: when many outcomes are examined, isolated nominal p-values are less persuasive unless the analysis plan specifies how multiplicity is handled. The registry record does not report a family-wise adjustment, hierarchical testing procedure, or other multiplicity strategy for the secondary outcomes. Their role is consequently supportive or exploratory rather than a substitute for the primary analysis. They may help describe the broader outcome profile, but they do not override the sponsor's primary analysis or resolve its discrepancy with the unadjusted recalculation.

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

• Virologic Response at Week 48 (Viral Load Less Than 400 Copies/mL)
• Change in log10 Viral Load From Baseline at Week 48
• Time to Reach First Virologic Response
• Time to Loss of Virologic Response
• Time-averaged Difference (DAVG) of log10 Plasma Viral Load Over 48 Weeks
• Change in CD4+ Cell Count From Baseline
• Change From Baseline in Total Functional Assessment of HIV Infection (FAHI) Score
• Percentage of Participants Adherent/Non-adherent to ARV as Determined by Modified Medication Adherence Self Report Inventory (M-MASRI) Questionnaire at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

General statistical context: random assignment is intended to make treatment groups comparable on average with respect to both measured and unmeasured baseline characteristics. It supports causal interpretation of a between-group contrast when the trial is conducted and analyzed as planned, but it does not guarantee that every realized group characteristic is identical. The registry identifies the study as randomized but does not report details of the randomization sequence, concealment procedures, or stratification factors. Those details are not reported in the registry record.

How is a binary response compared?

The primary outcome classifies each participant as a responder or nonresponder. A proportion is the number classified as responders divided by the number in the relevant group. A risk difference expresses the contrast as a subtraction of group proportions; a ratio measure instead compares them multiplicatively. General statistical context: the risk difference is often useful for understanding an absolute contrast, whereas ratio measures answer a relative question. The methods are not interchangeable, and the choice can affect both the numerical value and the way uncertainty is communicated.

The posted recalculation is an unadjusted comparison based on arm-level summaries. It does not reproduce a regression model with covariate adjustment. The registry's reported primary method is logistic regression, with the parameter described as a difference in proportion of response. The reported sponsor estimate and the simple recalculation differ, and the record flags that discrepancy. The sponsor's own analysis takes precedence; the recalculation is best treated as a limited check rather than as a replacement for the analysis specified and conducted by the sponsor.

What does a p-value say?

General statistical context: a p-value describes how incompatible the observed data, or more extreme data, are with a particular null hypothesis under the assumptions of the statistical model. It does not give the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The primary sponsor p-value is reported as p < 0.001 within an analysis classified as non-inferiority or equivalence. Without the margin and full testing specification, that p-value cannot independently establish how the sponsor's decision rule was defined. The recalculated unadjusted p-value addresses a different calculation and should not be substituted for the sponsor's analysis.

Why does the endpoint algorithm matter?

The TLOVR algorithm turns repeated viral-load observations and participant follow-up into a response classification. The registry requires confirmation at two consecutive visits for response and loss of response, treats permanent discontinuation as nonresponse after stopping, and defines how intermittent missing values are handled. It also counts resuppression after confirmed virologic failure as failure. General statistical context: such rules can influence the estimand, meaning the treatment contrast the analysis is intended to describe. Different rules for discontinuation, missing values, or failure could produce a different binary endpoint even if the observed laboratory measurements were unchanged.

The population is described as intention to treat. General statistical context: an intention-to-treat approach aims to retain participants in the groups to which they were assigned, preserving the benefits of randomization. The registry's explicit discontinuation rule is consistent with classifying outcomes after discontinuation rather than simply excluding those participants. The record does not report a separate per-protocol analysis or additional sensitivity analyses for the primary outcome; those analyses are not reported in the registry record.

How are time-to-event outcomes different?

Time-to-event methods account for both the time until an event and the fact that some participants may not experience the event during observed follow-up. The registry reports a Cox proportional hazards analysis for time to first virologic response. General statistical context: a hazard ratio compares instantaneous event rates among participants still at risk, under the model's assumptions; it is not a direct comparison of median times or a risk difference. The registry reports the Cox method but does not report diagnostics for the proportional-hazards assumption or details of censoring. These are not reported in the registry record.

The time-to-loss outcome also has a sponsor-reported Cox analysis, while the simple recalculation uses a mean difference in days. Those are different summaries with different interpretations. A mean difference in time and a hazard ratio should not be treated as estimates of the same quantity. The difference between them is particularly important when event times are censored or when the distribution of times is not well represented by a simple mean.

How should multiple outcomes be considered?

The registry lists primary and secondary outcomes covering several related but nonidentical aspects of response, immune status, function, and adherence. General statistical context: testing many outcomes increases the chance of seeing an apparently notable finding by chance if each test is interpreted in isolation. Methods such as hierarchical testing or adjustments to significance thresholds can address multiplicity, but the registry record does not report a multiplicity strategy. The sponsor's non-inferiority analysis of the primary endpoint should therefore be distinguished from exploratory reading across multiple secondary outcomes.

The original sample-size justification, non-inferiority margin, and detailed statistical analysis plan are not reported in the registry record. Those details would be needed to assess how the trial was designed for its stated objective, how the primary model was specified, and how missing or unusual observations were handled beyond the rules explicitly described for TLOVR.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimate under the assumptions of the analysis. General statistical context: it describes a range of values reasonably compatible with the data and model; it is not a range guaranteed to contain the true effect, nor is it a direct probability statement about the effect. Width matters: a narrower interval generally indicates greater precision, while a wider interval leaves more uncertainty about the size and direction of an effect.

The unadjusted primary recalculation reports a risk difference of -0.012 with a 95% confidence interval from -0.084 to 0.061. This interval crosses zero, so the simple recalculation is compatible with differences favoring either group under that measure. It also spans a substantial range of possible absolute differences. It should not be read as evidence of equivalence: equivalence or non-inferiority requires a prespecified margin, and that margin is not reported in the registry record.

The sponsor's reported primary estimate is 0.002, with a 95% confidence interval from -0.054 to 0.092. The reported analysis is categorized as non-inferiority or equivalence, but the registry record does not give the margin needed to judge the interval against the decision boundary. The sponsor's analysis takes precedence over the recalculation because the record flags a discrepancy. The distinct estimates and intervals should remain clearly separated rather than being blended or selectively compared.

For other outcomes, interval interpretation depends on the measure: a hazard-ratio interval concerns a relative event rate under a time-to-event model, whereas an interval for a mean difference concerns an average contrast. Neither is a general-purpose measure of precision for every clinical consequence. General statistical context: statistical precision is also distinct from clinical importance. The registry record does not identify thresholds for clinically meaningful differences for these outcomes, so interval width alone cannot establish whether a possible effect would be important to participants.

Confidence intervals do not correct for multiple comparisons unless the method explicitly accounts for multiplicity. The registry record does not report such an adjustment. Accordingly, intervals from secondary analyses should be read with their individual outcome definitions, methods, and multiplicity context in mind.

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 illustrations describe hypothetical future planning based on fractions of the observed effect, not the trial's original design. For the binary outcomes, the figures are participants per arm. For the time-to-event outcome, the figures are total events, not participants per arm. The distinction matters: an event target is not a participant target, because the number of events observed depends on follow-up and event occurrence.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report whether these were the assumptions used in the original trial design; these are planning assumptions for the illustrations only. The time-to-event illustrations use the Schoenfeld method and report total events.

The 80% power column represents the planned number of participants per arm, or total events for time-to-event analyses, under which a study would have an 80% chance of detecting the specified effect at the stated significance level if the assumptions hold. The 90% column represents a higher chance of detecting that same specified effect, and generally requires a larger planned study. These are prospective design probabilities under a model, not probabilities that the treatment is effective.

Rows that plan for 75% or 50% of the observed effect use smaller effects than the row planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation and therefore require more participants or events under the same assumptions. Because the observed effect is itself uncertain, using it as the basis for planning is only an illustration, not a guarantee that a future effect will match it. This is not observed power.

For the primary endpoint, the planning values are unusually large relative to the trial's enrolled population, reflecting the very small observed difference used in this calculation. They should not be interpreted as a recommendation or as evidence that the original trial was underpowered for its formal non-inferiority objective. The original design assumptions and non-inferiority margin are not reported in the registry record.

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 = 0.721; treatment proportion p₁ = 0.709; average p̄ = 0.715.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6382 = 1.2509.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6382 = 0.5371.
4. n = (1.2509 + 0.5371)² / (-0.0116)² = 23,639.2, rounded up to 23,640 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 <- 0.72108843537415                          # control proportion
p1 <- 0.709459459459459                          # 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(524368)
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 = 23,640 (80% power), 31,646 (90% power)
 75% of observed effect: n per arm = 41,897 (80% power), 56,088 (90% power)
 50% of observed effect: n per arm = 93,976 (80% power), 125,806 (90% power)
power.prop.test: 23639.2 
Simulated power at n = 23,640 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis using logistic regression for the primary endpoint, with the parameter described as a difference in response proportions. The sponsor estimate is 0.002, its 95% confidence interval runs from -0.054 to 0.092, and the reported p-value is p < 0.001. The registry classifies this as a non-inferiority or equivalence analysis.

A separate recalculation from the posted arm summaries is unadjusted and yields a different estimate and uncertainty interval. The record explicitly flags a discrepancy. Under that circumstance, the sponsor's own analysis takes precedence for the trial's reported result; the recalculation should be viewed as an independent arithmetic check using summary data, not as a correction to the sponsor's model. The registry record does not explain why the estimates differ, so the cause should not be inferred.

The sponsor's categorization does not by itself allow a reader to verify the non-inferiority conclusion. Such a conclusion depends on a prespecified margin and the relationship between that margin and the confidence interval. The non-inferiority margin is not reported in the registry record. The sponsor's reported analysis can therefore be described faithfully, but its decision rule cannot be independently reconstructed from the information recorded.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis is described as an intention-to-treat analysis, and the registry gives explicit TLOVR rules for classifying outcomes. Permanent discontinuation was treated as nonresponse after discontinuation. Intermittent missing viral-load values were treated as response when the preceding and succeeding visits indicated response; otherwise, they were imputed as nonresponse. Resuppression after confirmed virologic failure counted as failure. These rules define how incomplete or changing response histories contribute to the primary endpoint.

Those details do not constitute a full account of missing-data handling for every outcome. The registry record does not report sensitivity analyses under alternative missing-data assumptions, or a separate per-protocol analysis for the primary endpoint. Handling of missing observations for secondary outcomes is not reported in the registry record. The consequences of missingness may differ across binary, continuous, and time-to-event measures, so the primary endpoint rule should not be assumed to apply to every analysis.

The record lists multiple secondary outcomes and reports analyses for several different measures. It does not report a multiplicity-control plan, such as a hierarchy among outcomes or an adjustment to account for testing several hypotheses. General statistical context: without such a plan, a nominally small p-value among many tested outcomes can be less compelling than the same p-value for a single prespecified primary test. This does not make secondary results uninformative; it changes the strength of inference that can reasonably be attached to them.

The registry record does not report the original sample-size justification, the non-inferiority margin, interim-analysis procedures, or a complete statistical analysis plan. Those items would clarify how the primary objective was operationalized and how the study addressed repeated testing, missing outcomes, and alternative analysis populations. Their absence limits independent review, but it does not justify guessing what procedures were used.

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: pneumonia (1.0%), respiratory distress (0.7%), anaemia (0.7%), cardiac failure congestive (0.7%), anxiety (0.7%).

The registry reports serious adverse events for both treatment groups. There were 16 participants with serious adverse events in the once-daily group and 27 in the twice-daily group, with 294 and 296 participants respectively listed at risk. The registry also reports other adverse events affecting 134 participants in the once-daily group and 147 in the twice-daily group, with the same group-specific at-risk counts. These are descriptive counts; they are not, by themselves, adjusted comparisons of safety.

The most frequently listed serious-event terms include pneumonia at 1.0%, and respiratory distress, anaemia, congestive cardiac failure, and anxiety at 0.7% each. Appendicitis is listed at 0.3%. These terms describe reported serious events and should not be read as a complete account of every possible adverse event. The registry record does not report deaths for these groups.

General statistical context: event counts can be affected by follow-up duration, event definitions, and whether multiple events in one participant are counted separately. The record's figures should therefore be interpreted according to its reporting conventions; further detail on event adjudication and exposure-adjusted rates is not reported in the registry record. The counts do not establish that a regimen is safer or less safe.

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

The result describes a randomized comparison of two darunavir/ritonavir dosing schedules, each used with selected optimized background therapy, in early treatment-experienced participants with HIV-1. The primary outcome concerns the proportion meeting a defined viral-load response threshold at Week 48, with participant histories classified using TLOVR rules for confirmation, discontinuation, missing visits, and confirmed failure.

The sponsor reported a logistic-regression analysis classified as non-inferiority or equivalence, while an unadjusted recalculation from the posted arm summaries differs. The registry flags this discrepancy, so the sponsor's analysis takes precedence as the reported trial analysis. The non-inferiority margin is not reported in the registry record; as a result, readers cannot independently check the margin-based conclusion from the estimate, interval, and p-value alone.

The result does not establish that the two schedules are identical. A failure to detect a difference under a particular analysis is not proof of equivalence, and formal non-inferiority depends on a prespecified margin. It also does not show that one schedule is preferable for every participant, or that findings apply to people outside the population and treatment setting recorded in the trial.

The primary outcome is a virological measure, not a complete summary of safety, function, adherence, or long-term experience. Secondary outcomes can add information, but they use different definitions and statistical methods, and the registry record does not report a multiplicity strategy. The serious adverse-event counts are descriptive and should not be treated as a definitive comparative safety analysis.

General statistical context: estimates are most informative when considered together with their uncertainty, endpoint definition, analysis population, and prespecified decision rule. Here, the sponsor's analysis is the appropriate starting point for the trial's formal primary result, while the discrepancy, missing design details, and absence of the non-inferiority margin limit independent verification.

18. Why This Trial Matters Statistically

This trial illustrates why the label attached to an analysis matters. The primary outcome is binary, but the formal sponsor analysis uses logistic regression and is classified as non-inferiority or equivalence. A simple comparison of posted group summaries gives a different estimate. Those analyses cannot be treated as interchangeable: one is the sponsor's reported model-based analysis, and the other is an unadjusted recalculation.

It also highlights that a non-inferiority conclusion is not established merely by similar observed response counts or a small p-value. The conclusion depends on a prespecified margin and the analysis rule applied to it. Because the margin is not reported in the registry record, the reported conclusion cannot be independently checked against that boundary. This is a practical example of why registry results should be read alongside the statistical plan when available.

The TLOVR endpoint demonstrates how outcome construction involves more than selecting a laboratory threshold. Confirmation across visits, treatment discontinuation, intermittent missing values, and resuppression after confirmed failure all affect the final classification. Such rules are part of the estimand and can shape the apparent treatment contrast.

Finally, the record includes outcomes on viral suppression, response timing, immune status, function, adherence, and adverse events. Their differing measures and analysis methods resist a single summary claim. Recognizing this diversity, and the unreported multiplicity plan, helps keep secondary findings in their proper evidential role rather than treating each nominal result as an independent confirmation.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the non-inferiority margin, which is central to independently evaluating the primary non-inferiority or equivalence analysis. It also flags a discrepancy between the sponsor's analysis and the simple recalculation from arm summaries, without explaining the source. The sponsor's analysis takes precedence, but the difference limits the ability to verify the result from the posted summary statistics alone.

The record does not report the original sample-size justification, detailed statistical analysis plan, interim-analysis procedures, or a multiplicity strategy for secondary outcomes. It therefore does not permit a full assessment of the trial's power for its formal objective, planned testing sequence, or handling of multiple outcome comparisons. The planning illustrations based on observed effects are not a substitute for the original design rationale.

The trial was open-label. The primary endpoint is based on viral-load measurements, but open-label assignment could still influence co-interventions, adherence, discontinuation, or other processes that contribute to outcomes. The registry describes an intention-to-treat population and TLOVR rules, but does not report a separate per-protocol primary analysis or sensitivity analyses under alternate missing-data assumptions.

Some listed secondary outcomes are not accompanied by detailed numerical results in the statistical summary. Details of randomization procedures, masking of endpoint assessment, background-regimen selection, censoring rules for time-to-event analyses, and diagnostic checks for model assumptions are not reported in the registry record. These omissions do not show that the procedures were inadequate; they limit what can be assessed from the registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare Effectiveness and Safety of Darunavir/Ritonavir (DRV/Rtv) 800mg/100mg Once Daily Versus DRV/Rtv 600mg/100mg Twice Daily in Early Treatment-Experienced HIV-1 Infected Patients (ODIN) — NCT00524368.
• Registry record last updated 2013-02-15; status last verified 2013-02.
• Results first posted 2010-09-22.
• 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

The registry describes a completed randomized, open-label, parallel-group Phase 3 trial in early treatment-experienced participants with HIV-1. It compared darunavir/ritonavir 800/100 mg once daily with 600/100 mg twice daily, each alongside selected optimized background regimen therapy. Enrollment was 590.

The primary endpoint was Week 48 virological response, defined as plasma viral load below 50 copies/mL using the TLOVR algorithm. The posted response counts were 212 of 294 for once-daily treatment and 210 of 296 for twice-daily treatment. The sponsor reported a logistic-regression non-inferiority or equivalence analysis, but the registry does not report the margin. The record flags a discrepancy with the unadjusted recalculation, so the sponsor's analysis takes precedence.

Secondary outcomes address additional viral, immune, functional, adherence, and time-to-event measures. Serious adverse-event counts and selected event terms are also reported. The missing margin, unexplained analytical discrepancy, and unreported design and multiplicity details limit independent assessment of the formal conclusion.