Nine Month Course of Anti-HIV Medications for People Recently Infected With HIV: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nine Month Course of Anti-HIV Medications for People Recently Infected With HIV (NCT00090779), a randomized phase 2 study. The primary outcome is Ranked Log10 HIV-1 RNA Viral Load (log10 Copies/mL) Averaged at 72 and 76 Weeks for the IT Arm and DT Arm.

2. Clinical Question

This was a randomized Phase 2 study with an open-label design. Its central comparison was not simply a viral-load measurement taken at one visit: it combined later viral-load measurements with assigned ranks for participants who did not remain off antiretroviral therapy through the required visits. The registry description says the rank assignment was designed, if anything, to bias against finding a treatment effect.

The study also recorded outcomes concerning CD4 counts, treatment initiation or re-initiation, time to meeting criteria, and time to treatment initiation or death. Those outcomes address related but distinct questions. The posted primary comparison concerns the ranked viral-load outcome, while the available secondary numerical comparison concerns meeting criteria for treatment initiation or re-initiation.

3. Trial Design

The registry describes a randomized, parallel-group Phase 2 study with no masking. Its title identifies the comparison as immediate treatment with potent antiretroviral therapy versus observation with treatment as indicated in newly infected HIV-1 participants. The immediate-treatment arm is labeled IT; the deferred-treatment arm is labeled DT. Participants in the IT arm received emtricitabine/tenofovir disoproxil fumarate once daily and lopinavir/ritonavir twice daily. Participants in the DT arm received no treatment.

Enrollment was 130. The registry lists the study as terminated, with a start date of 2005-01 and primary completion in 2009-07. The reason for termination is not reported in the registry record. The registry does not report the planned sample-size justification or the statistical analysis plan in the information available for this analysis.

The primary endpoint analysis population was narrower than the full enrollment: it included participants in follow-up at least 72 weeks since randomization. The posted arm summaries include 39 participants in the IT arm and 40 in the DT arm. These endpoint denominators should not be read as the numbers randomized or as the safety denominators. For the adverse-event summaries, the at-risk groups were 66 in the IT arm and 64 in the DT arm. For the posted secondary treatment-criteria outcome, the denominators were also 66 and 64.

Because masking was absent, treatment assignment was known to participants and investigators. Randomization supports a comparison between assigned groups, but it does not remove every possible source of bias or uncertainty, especially when the endpoint includes decisions about treatment or entry into Step 2. The registry record does not report allocation concealment details, the method used to generate the random sequence, or further detail about how departures from assigned treatment were handled.

The design combines an immediate-treatment strategy with a deferred-treatment strategy. The latter was not simply an untreated control throughout the full study: the title and outcome definitions allow for treatment as indicated, and several secondary outcomes concern the point at which treatment criteria were met. This distinction matters when interpreting later viral-load values, because treatment initiation can affect whether a participant contributes an observed off-treatment viral-load measurement or an assigned rank.

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.

Step 1

Reasons for not completing this period:

Step 2

Reasons for not completing this period:

Step 3

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in follow-up at least 72 weeks since randomization were included.

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 Ranked Log10 HIV-1 RNA Viral Load (log10 Copies/mL) Averaged at 72 and 76 Weeks for the IT Arm and DT Arm, measured over At Weeks 72 and 76.

The primary endpoint was the ranked log10 HIV-1 RNA viral load, averaged at Weeks 72 and 76 for the IT and DT arms under different off-treatment follow-up rules. For the DT arm, the endpoint used the average viral load at Weeks 72 and 76 for participants who continued to Week 72 off antiretroviral therapy. For the IT arm, it used the average at Weeks 72 and 76 for participants who continued to Week 36 off therapy. Participants who needed antiretroviral therapy or met criteria for Step 2 before the relevant visits were treated as endpoint failures and assigned a rank.

The registry description says a failure's assigned rank was either the last observed rank carried forward or the worst rank relative to other possible outcomes. Its example explains that carrying forward an earlier rank preserves that participant's position in the ordering rather than discarding the participant for lacking the later off-treatment measurements. The description also says this approach was designed, if anything, to bias against finding a treatment effect.

A rank endpoint compares relative ordering rather than presenting the result in the original log10 viral-load units. The reported medians are 26 for IT and 49.3 for DT, with full ranges of 1 to 70 and 4 to 70, respectively. These values are ranks, not viral-load concentrations. A rank-based endpoint can accommodate a specified ordering of outcomes that includes early treatment or Step 2, but its interpretation depends on those ranking rules. The registry record does not report a confidence interval for the primary comparison.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

A statistical method is most useful when its target is clear. In this study, the primary target was a ranked endpoint assembled from later viral-load measurements and assigned ranks for specified failures. The sponsor compared the arm distributions using the Wilcoxon (Mann-Whitney) method. That test evaluates whether observations from one group tend to occupy different positions in the combined ordering than observations from the other group. It does not require the comparison to be expressed as a difference between means, and it does not directly estimate a difference in viral-load units.

Why use ranks?

Ranks replace the original numerical values with their order in the combined set. This can be useful when the endpoint is defined through ordering, when distributions may not be well represented by a mean-and-standard-deviation summary, or when outcomes include an ordered category such as a failure rank. Here, ranking allowed participants who met treatment or Step 2 criteria before the planned viral-load visits to remain part of the primary endpoint through assigned ranks.

The median ranks and full ranges describe each arm separately. The median indicates the middle position in the arm's rank distribution; the range gives its observed lowest and highest ranks. Neither summary alone describes the uncertainty in the between-arm comparison. A confidence interval for an effect estimate would add information about precision, but the registry record does not report one for the primary result. The sponsor's p = 0.005 is the reported inferential result for the Wilcoxon comparison.

What does the p-value say?

In general, a p-value measures how unusual data at least as incompatible with a stated null hypothesis would be if that null hypothesis and the test assumptions held. A small p-value is not the probability that the null hypothesis is true, nor is it a measure of the magnitude or practical importance of an effect. For the primary endpoint, the p-value should be interpreted in relation to the particular rank construction and the participants included in that analysis. The registry does not report a primary confidence interval or enough detail to reconstruct one from the posted summaries.

How to read the secondary comparison

The treatment-criteria outcome is a binary measure: each participant either met the stated criteria during the follow-up period or did not. The posted counts are 7 of 66 in IT and 23 of 64 in DT. The recalculated risk difference is 0.253 for DT relative to IT, with a 95% confidence interval from 0.114 to 0.392. In general, a risk difference expresses the difference between two event proportions on the probability scale. Its confidence interval gives a range of values compatible with the data and the calculation method, subject to its assumptions.

The same recalculation reports a risk ratio of 3.388 with a 95% confidence interval from 1.564 to 7.34, and an odds ratio of 4.728 with a 95% confidence interval from 1.856 to 12.05. These are distinct effect measures: a risk ratio compares event probabilities, while an odds ratio compares event odds. They are not interchangeable with the risk difference, and each communicates the contrast on a different scale. The unadjusted p-value is p < 0.001. These recalculated estimates are simple, unadjusted comparisons based on the posted summary counts, not substitutes for a sponsor analysis.

Why over-dispersion can matter

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model assumes less variability than the data contain, it can produce uncertainty estimates that are too narrow and tests that are too optimistic. The primary analysis is a rank-based comparison rather than a reported count model, so over-dispersion is not a reported feature of its analysis. For binary or count outcomes in other settings, researchers should check whether the model's variance assumptions fit the observed data. The registry record does not report a model-based adjustment for over-dispersion for these results.

Planning illustrations are not trial power

The planning illustrations use the observed secondary risk difference as a starting point and show hypothetical participants per arm for selected fractions of that observed effect. Under the listed assumptions, planning for 100% of the observed effect gives 43 participants per arm for 80% power and 57 participants per arm for 90% power. Planning for 75% of the observed effect gives 69 participants per arm for 80% power and 92 participants per arm for 90% power. Planning for 50% of the observed effect gives 137 participants per arm for 80% power and 183 participants per arm for 90% power.

These are planning illustrations, not observed power and not a reconstruction of the trial's design. The stated assumptions are a two-sided significance level of 0.05, equal allocation, and a normal approximation. The registry record does not report that these assumptions were used to plan the study, nor does it report the trial's own sample-size justification. Planning from an observed effect can be optimistic because the observed effect is itself uncertain; the illustrations are best understood as conditional scenarios rather than promises about future studies.

10. Analyses Reported by the Sponsor

For the primary ranked viral-load endpoint, the registry reports the sponsor's Wilcoxon (Mann-Whitney) analysis, with p = 0.005. No recalculated primary effect estimate or confidence interval is reported in the available record. The primary medians and ranges are summaries of ranks, and they do not provide enough information to reconstruct the sponsor's comparison or its uncertainty independently.

The separate recalculation concerns the secondary count of participants meeting criteria for treatment initiation or re-initiation. It uses the posted counts of 7 of 66 in IT and 23 of 64 in DT to give an unadjusted risk difference, confidence interval, risk ratio, odds ratio, and p-value. This calculation does not re-analyze the primary rank endpoint and does not replace the sponsor's primary test.

No discrepancy between sponsor results and recalculated results is flagged in the registry record. The two sets of statistics address different outcomes, so agreement in their general direction is not a formal replication of the same analysis. The sponsor's primary analysis remains the reported inferential result for the primary endpoint; the simple secondary recalculation is supplementary and does not account for covariates or multiplicity.

11. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists several secondary outcomes. It does not report a multiplicity strategy, such as a prespecified testing hierarchy or adjustment across outcomes. Without that information, the secondary results should be interpreted as exploratory or supportive rather than as a collection of independent confirmatory conclusions. This is especially relevant when several outcomes, time points, or analysis choices are examined, because repeated testing can make chance findings more likely.

The primary endpoint description does specify how certain failures were incorporated into the ranking. For participants who needed antiretroviral therapy or met criteria for Step 2 before the relevant visits, the assigned rank was either the last observed rank carried forward or the worst rank relative to other possible outcomes. The description says this approach was designed, if anything, to bias against finding a treatment effect. The registry does not give further detail about how the choice between those rank assignments was made for each participant.

The endpoint population included participants in follow-up at least 72 weeks since randomization. The reported primary denominators were 39 in IT and 40 in DT, whereas the treatment-criteria and adverse-event summaries use 66 and 64, respectively. The registry record does not report a complete account of missing observations, reasons for participants not contributing to the primary endpoint, or sensitivity analyses for missing data. It also does not state whether the primary comparison followed an intention-to-treat principle or describe how other treatment changes were handled.

The title and endpoint descriptions make clear that treatment initiation could occur during follow-up, and the primary rank procedure accounts for some early failures. However, further information about adherence, protocol deviations, and the handling of all post-randomization events is not reported in the registry record. These omissions limit assessment of how robust the conclusions are to alternative missing-data or analysis-population assumptions.

The registry record also does not report the primary analysis's confidence interval, a detailed statistical analysis plan, or interim-analysis procedures. The planning illustrations use stated assumptions for hypothetical sample-size scenarios, but they are not evidence of the trial's original design assumptions or its observed power.

12. 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: blood bilirubin increased (1.5%).

The adverse-event summaries report serious adverse events in 1 of 66 participants in the IT arm and 0 of 64 in the DT arm. The registry lists Blood bilirubin increased at 1.5% among the top serious adverse-event terms, but the available information does not identify an arm for that term. These counts are descriptive; the registry does not report a statistical comparison of serious adverse events or a confidence interval for the difference between groups.

The record also reports other adverse events in 58 of 66 participants in IT and 48 of 64 in DT. These are listed separately from serious adverse events and should not be read as serious-event counts. The deaths field is not populated in the available record, so death counts are not reported in the registry record.

Adverse-event counts can help describe what was recorded during the study, but sparse events make comparisons imprecise. Differences in counts alone do not establish a causal safety difference, and the available summaries do not provide event timing, duration, relatedness, or a complete clinical account. These figures should be read as registry summaries, not as a comprehensive safety assessment.

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

The primary result shows a statistically significant difference in the ranked viral-load outcome between the randomized arms under the registered endpoint definition: the sponsor reported p = 0.005 for the Wilcoxon (Mann-Whitney) comparison. The IT median rank was 26 and the DT median rank was 49.3. Because ranks are relative positions and the endpoint assigns ranks to specified failures, these summaries do not quantify a difference in viral load on the original log10 scale.

The separate secondary result shows a difference between the arms in the number of participants meeting clinical, virologic, or immunologic criteria for treatment initiation or re-initiation by 96 weeks since randomization. Its unadjusted recalculation gives a risk difference of 0.253 for DT relative to IT, with a 95% confidence interval from 0.114 to 0.392. That finding concerns a treatment-criteria outcome, not the primary viral-load ranking, and it does not by itself explain why participants met criteria.

The results do not establish the size of a clinical benefit or harm, and the registry summaries do not provide a confidence interval for the primary rank comparison. They also do not explain the reason the study was terminated, provide a full account of missing data, or document the complete statistical analysis plan. The primary endpoint's rank assignment rules and the different analysis denominators should remain part of any interpretation.

Statistical evidence from this study should not be treated as a treatment recommendation. The trial results describe group comparisons within the reported study design and populations. They do not determine what is appropriate for an individual, and they do not establish that the same comparison would produce the same results in other populations or settings.

14. Why This Trial Matters Statistically

This trial illustrates why endpoint construction matters. A simple comparison of viral-load measurements at later visits could exclude participants who started treatment or entered Step 2 before those visits. The registered primary endpoint instead assigned ranks to specified failures, allowing the analysis to represent both later observed viral-load averages and some earlier events in a single ordered outcome. That approach preserves information, but it also means the rank rules are central to what the primary test means.

The study also illustrates the distinction between statistical significance and effect interpretation. The sponsor's p = 0.005 indicates evidence of a difference in the ranked distributions under the chosen test, but the reported medians and ranges are ranks rather than viral-load concentrations. No primary confidence interval is reported, limiting direct assessment of precision for the between-arm comparison.

Different denominators across outcomes matter as well. The primary endpoint uses participants in follow-up at least 72 weeks after randomization, while secondary and safety summaries use larger at-risk groups. These analyses answer related but distinct questions and should not be combined as if they drew on identical populations.

Finally, the record separates an explicitly designated primary endpoint from multiple secondary outcomes, yet does not report how multiplicity was handled. That distinction is important when interpreting supporting findings: a secondary result may add context, but it does not automatically carry the same evidential status as the primary analysis. Together, these features make the study a useful example of reading endpoint definitions, analysis populations, test results, and reporting gaps as parts of one statistical interpretation.

15. 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 primary outcome is a constructed rank rather than a direct summary in log10 viral-load units. Its interpretation depends on the rules for failures, including carrying forward a last observed rank or assigning the worst rank relative to other possible outcomes. The registry does not report the participant-level application of those alternatives or provide a primary confidence interval, limiting independent assessment of effect magnitude and precision.

The analysis population for the primary endpoint consisted of participants in follow-up at least 72 weeks since randomization, with reported denominators of 39 in IT and 40 in DT. The full enrollment was 130. The reasons for the smaller primary endpoint denominators and the handling of missing observations are not reported in the registry record. The record also does not describe the full analysis population rules or report sensitivity analyses.

The study was unmasked, and the comparator strategy allowed treatment as indicated. Outcomes involving treatment criteria can depend on clinical, virologic, or immunologic assessments and decisions during follow-up. The registry does not provide further information about assessment procedures, adherence, allocation concealment, or how all treatment changes were handled. These limitations affect interpretation of both the primary rank endpoint and related treatment-initiation outcomes.

The registry lists multiple secondary outcomes but does not report a multiplicity plan in the available record. It also does not report the sample-size justification, interim-analysis procedures, or the reason for termination. The posted planning illustrations are based on an observed secondary effect and are not the trial's design justification. Consequently, those illustrations cannot resolve uncertainty about the study's original power assumptions or the confirmatory status of the secondary findings.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Nine Month Course of Anti-HIV Medications for People Recently Infected With HIV — NCT00090779.
• Registry record last updated 2018-10-11; status last verified 2018-09.
• Results first posted 2012-12-18.
• 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.

19. Record Summary

NCT00090779 is a randomized, open-label, parallel-group Phase 2 study of immediate versus deferred antiretroviral treatment in newly infected HIV-1 participants. Enrollment was 130; the registry lists the study as terminated. The immediate-treatment arm received emtricitabine/tenofovir disoproxil fumarate once daily and lopinavir/ritonavir twice daily, while the deferred-treatment arm received no treatment.

The primary outcome was ranked log10 HIV-1 RNA viral load averaged at Weeks 72 and 76 under specified off-treatment and failure-rank rules. The sponsor reported median ranks of 26 for IT and 49.3 for DT and a Wilcoxon (Mann-Whitney) p-value of 0.005. A secondary treatment-criteria outcome has a separate unadjusted recalculation. The record does not report a primary confidence interval, a multiplicity plan, or the reason for termination.