Immediate Versus Deferred Start of Anti-HIV Therapy in HIV-Infected Adults Being Treated for Tuberculosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Immediate Versus Deferred Start of Anti-HIV Therapy in HIV-Infected Adults Being Treated for Tuberculosis (NCT00108862), a randomized phase 4 study. The primary outcome is Percent of Participants Who Survived Without AIDS Progression..

2. Clinical Question

The study was designed around a timing decision rather than a comparison of different antiretroviral medicines. Its stated hypothesis was that immediate therapy would reduce the frequency of other AIDS-defining illnesses and death by at least 40% at week 48 compared with deferred therapy. That is the study’s hypothesis, not a result established by the posted outcome values.

The primary outcome description says participants were followed for 48 weeks whether they began antiretroviral therapy as scheduled, began it at all, or discontinued tuberculosis treatment, including because they did not have tuberculosis. This makes the question one about the assigned strategies as implemented in the trial, rather than the effect only among people who adhered to the assigned start time. The posted primary outcome is labeled as the percent surviving without a new AIDS-defining illness, but the arm percentages and event counts do not straightforwardly align with that wording. The registry record does not explain this apparent inconsistency, so the endpoint’s direction should be read cautiously.

3. Trial Design

This was a randomized, parallel-group, phase 4 study with no masking. The registry lists enrollment as 809 and the study status as completed. The study start is recorded as 2006-08, and primary completion as 2010-07. The two assigned strategies were immediate antiretroviral therapy after approximately 2 weeks of tuberculosis treatment and deferred therapy after 8 to 12 weeks.

The primary endpoint was assessed through week 48. The registry describes an intent-to-treat approach: participants were analyzed according to randomized strategy, ignoring changes from that assignment. The endpoint description also says follow-up continued regardless of whether antiretroviral therapy was started as scheduled, started at all, or whether tuberculosis treatment was discontinued. Thus, the estimand implied by the description is a comparison of assignment strategies, not a comparison limited to participants who followed the planned timing.

The registry identifies Kaplan-Meier estimation and an associated standard error for the primary outcome. It also reports a two-sided Z-test for a mean difference in final values. Those methods are not described in enough detail to reconstruct every element of the sponsor’s analysis, including the precise handling of censoring or the relationship between the reported test and the Kaplan-Meier estimates.

The registry record does not report the original sample-size justification, the trial’s planned significance level or target power, interim analyses, or a detailed statistical analysis plan. The planning figures associated with the observed results are separate illustrations and should not be mistaken for the trial’s original design assumptions. Details such as stratification factors, allocation procedures, or additional protocol deviations are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: HIV-infected persons at least 13 years of age, naive to antiretroviral therapy, who had received 1-14 cumulative days of a rifamycin-based TB regimen within 28 days prior to study entry, and had a CD4 count \<250 cells/mm3. Randomization was stratified by screening CD4 (\<50 vs =\>50). Three participants were deemed ineligible and taken off study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Numbers presented use the intent-to-treat approach (i.e., ignoring changes from randomized treatment strategy).

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 Percent of Participants Who Survived Without AIDS Progression., measured over Through week 48.

The primary outcome is labeled as the percent of participants who survived without AIDS progression through week 48. The description defines this in terms of remaining alive without a new AIDS-defining illness, and says it was estimated with a Kaplan-Meier method and an associated standard error. In general, Kaplan-Meier estimation is used to describe the probability of remaining free of an event over follow-up while accounting for the timing of observed events and censoring.

An endpoint combining survival and AIDS progression is clinically and statistically relevant to the trial’s stated question because it captures more than one important outcome during the treatment period. The registry’s intent-to-treat description also ties the endpoint to the assigned treatment-start strategy, even if a participant did not follow that strategy exactly.

There is an important reporting ambiguity. The endpoint title says survival without AIDS progression, while the posted arm values are 13% for immediate ART and 16% for deferred ART, and the comparison calculation uses event proportions of 0.131 and 0.160. The record does not explain how those percentages relate to the endpoint wording. Therefore, the percentages should not be reinterpreted as a clear estimate of the probability of remaining alive and progression-free without resolving that ambiguity. The posted result can be described, but its direction and meaning require caution.

7. Results Posted in the Registry

• Deferred ART: 16.0% (64/401) versus 13.1% (53/405) on control; risk difference 2.9 percentage points (95% CI -2.0 to 7.7), risk ratio 1.22 (0.87–1.71); unadjusted two-proportion z-test p = 0.247.

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.

Percent of Participants With Culture-confirmed Tuberculosis (TB) Who Survived Without AIDS Progression.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Deferred ART: 17.1% (31/181) versus 11.9% (23/193) on control; risk difference 5.2 percentage points (95% CI -1.9 to 12.4), risk ratio 1.44 (0.87–2.37); unadjusted two-proportion z-test p = 0.152.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferred ART and the control. The interval gives the range of effects that remain compatible with the data.

Percent of Participants With MTB IRIS.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Deferred ART: 5.0% (20/401) versus 11.1% (45/405) on control; risk difference -6.1 percentage points (95% CI -9.9 to -2.4), risk ratio 0.45 (0.27–0.75); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Deferred ART than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent of Participants With HIV IRIS.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Deferred ART: 3.0% (12/401) versus 3.0% (12/405) on control; risk difference 0.0 percentage points (95% CI -2.3 to 2.4), risk ratio 1.01 (0.46–2.22); unadjusted two-proportion z-test p = 0.980.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferred ART and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover additional clinical and laboratory events, tuberculosis outcomes, immune recovery, and immune reconstitution inflammatory syndrome. They broaden the descriptive picture beyond the primary endpoint, but they do not replace the primary strategy comparison. Across the reported secondary results, the numerical pattern is not uniform: some comparisons are close, while others show more separation. This variation is expected when several outcomes are examined and should not be compressed into a single claim about the overall effect of either strategy.

The culture-confirmed tuberculosis subgroup outcome is related to the primary question but applies to a narrower population than the overall randomized comparison. The registry also reports MTB IRIS and HIV IRIS separately. These outcomes concern specific events and do not directly settle the broader question of survival without AIDS progression. They should be read as secondary, outcome-specific observations rather than as confirmatory substitutes for the primary result.

The registry record lists multiple secondary outcomes, and the posted secondary analyses include unadjusted comparisons. When many endpoints are examined, the chance of at least one apparently unusual result arising by chance can increase. Without a reported multiplicity plan, isolated secondary p-values carry less evidential weight than a prespecified primary analysis. The record does not report whether these secondary comparisons were adjusted or designated for formal hypothesis testing.

Secondary outcomes can still be useful for describing the range of events assessed and for identifying questions that might warrant further study. Their interpretation should account for their population definitions, endpoint-specific uncertainty, and the absence of reported multiplicity procedures. They do not resolve the primary endpoint’s wording ambiguity or establish a general conclusion about treatment timing.

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

• Percent of Participants Reporting a Grade 3 or 4 Adverse Event or Laboratory Abnormality
• Time to First New AIDS-defining Illness or Death.
• Percent of Participants With Culture-confirmed Tuberculosis (TB) Who Survived Without AIDS Progression.
• Percent of Participants Who Interrupted or Discontinued at Least One Tuberculosis (TB) Medication Due to Toxicity.
• Percent of Participants With Confirmed or Probable Tuberculosis (TB) Whose TB Resolved, or Who Required TB Treatment Through the End of Follow-up, or Died, or Were Lost to Follow-up.
• Percent of Participants Whose CD4 Increased by at Least 100 Cells/mm^3 Between Baseline and Week 48.
• Percent of Participants With MTB IRIS.
• Percent of Participants With HIV IRIS.

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary endpoint estimate?

The registry describes the primary endpoint as the percent of participants who survived without a new AIDS-defining illness through week 48. It says the percent was calculated with a Kaplan-Meier estimator and an associated standard error. In general, Kaplan-Meier estimation is useful when follow-up time matters and participants may have different observation periods. It estimates event-free experience over time while accounting for censoring under assumptions about why follow-up ends. The registry record does not describe the censoring rules, the number censored, or the assumptions used in detail.

The endpoint description says that all eligible randomized participants were followed whether or not they began ART on schedule, began ART at all, or continued tuberculosis treatment. This is consistent with an intent-to-treat strategy comparison. The record states that changes from randomized treatment strategy were ignored in the analysis. This preserves the comparison defined by random assignment, but it does not estimate the effect of actually starting ART at a particular time among only those who adhered.

How should the recalculated comparison be read?

The posted recalculation uses the arm-level event proportions to express a risk difference, with deferred ART compared against immediate ART. The estimate is 0.029, its 95% confidence interval is -0.020 to 0.077, and its unadjusted p-value is 0.247. A risk difference is the difference between two proportions on the absolute scale. In general, a value of zero corresponds to equal proportions; a confidence interval spanning zero indicates that the estimate is compatible with differences in either direction as well as no difference, at the interval’s stated confidence level.

This recalculation is simple and unadjusted. It is not the same as reproducing a Kaplan-Meier analysis with individual follow-up times. The underlying event proportions and denominators are posted, but the individual event times and censoring information are not reported in the registry record. In addition, the endpoint title and the event proportions appear difficult to reconcile. The recalculated direction should therefore not be translated into a confident claim about which strategy produced more survival without progression.

What does the sponsor’s test add?

The registry reports a two-sided Z-test with a mean difference in final values of 3, a confidence interval from -2 to 8, a stated confidence level of 95.08%, and p = 0.45. A two-sided test considers departures in either direction. In general, a p-value describes how incompatible the observed data are with a specified null model, assuming the test’s model and assumptions apply; it is not the probability that the null hypothesis is true. A confidence interval describes a range of values compatible with the estimate and method, not a guarantee that the true value lies within the interval.

The sponsor result and the recalculated risk difference are not identical summaries: one is reported as a mean difference in final values, while the recalculation is an unadjusted risk difference. The registry record does not fully explain their relationship. The calculations should be presented as distinct analyses rather than combined into a single estimate.

Why can over-dispersion matter?

In general, a simple binary-outcome model often assumes that variability follows the binomial distribution given the event probability and group size. Over-dispersion means observed variation is greater than that model expects. If it is present and ignored, standard errors can be too small and confidence intervals too narrow. The registry record does not report an over-dispersion assessment or a model that accounts for it. The primary endpoint’s stated Kaplan-Meier approach is not enough to infer whether over-dispersion was considered in other analyses.

What is and is not reported about the analysis plan?

The registry record does not report the original sample-size justification, planned power, interim monitoring, multiplicity adjustment, detailed missing-data procedures, or a full statistical analysis plan. It identifies the primary analysis as intent-to-treat and names Kaplan-Meier estimation, but does not supply the detailed assumptions required to reproduce that analysis. The planning illustrations associated with the observed effects use a two-sided significance level of 0.05, equal allocation, and a normal approximation; those are assumptions for the illustrations, not confirmed assumptions of the original trial design.

11. Confidence Intervals and Precision

The primary arm-level estimates are 13% for immediate ART, with a 95% confidence interval of 10% to 16%, and 16% for deferred ART, with a 95% confidence interval of 12% to 20%. These intervals describe uncertainty around each reported arm estimate. Their overlap is not, by itself, a formal test of the difference between arms; the direct recalculated comparison is more relevant for that question.

For deferred versus immediate ART, the recalculated risk difference is 0.029, with a 95% confidence interval from -0.020 to 0.077. Because the interval includes zero and extends in both directions, the posted results are compatible with no difference as well as with differences favoring either direction on the recalculation’s scale. The interval’s width means that the estimate is not highly precise. The unadjusted p-value of 0.247 is consistent with that uncertainty, but the p-value does not measure the size or clinical importance of an effect.

The sponsor’s reported mean difference is 3, with a confidence interval from -2 to 8 and a stated confidence level of 95.08%. This interval also includes zero. It is a separate analysis with a different reported measure, so its precision should not be treated as interchangeable with the recalculated risk difference.

These statistical intervals do not resolve the endpoint-label ambiguity. The registry’s description of survival without progression does not straightforwardly match the posted percentages and event proportions. Precision around a numerical estimate cannot fix uncertainty about exactly what that estimate represents. The record also does not report the detailed censoring information or missing-data handling needed to independently assess the Kaplan-Meier estimate.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For this binary outcome, the figures are participants per arm, not total events. The stated planning 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. These assumptions are for interpreting the planning display; the original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column means the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and model were correct. The 90% power column uses a higher target chance of detecting that specified effect and therefore generally requires more participants per arm. This is a design-planning interpretation, not a claim about the probability that the study’s conclusion is correct.

Rows for planning for 75% or 50% of the observed effect consider smaller effects than planning for the full observed effect. Smaller effects are harder to distinguish from random variation, so more participants are generally needed to achieve the same target power. The displayed figures should be read as conditional planning scenarios, not as evidence that the observed effect is stable or that a future study would reproduce it.

This is not observed power. Observed power is sometimes calculated from the effect estimate after a study, but it does not provide an independent measure of how persuasive or precise the result is. The confidence interval and the reported analyses are more informative for interpreting the uncertainty in this trial. The curve is a visual way to read how required sample size changes with the assumed effect; it does not add evidence about the trial’s actual treatment effect.

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 = 0.131; treatment proportion p₁ = 0.160; average p̄ = 0.145.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4983 = 0.9766.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4979 = 0.4190.
4. n = (0.9766 + 0.4190)² / (0.0287)² = 2,358.6, rounded up to 2,359 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 <- 0.130864197530864                          # control proportion
p1 <- 0.159600997506234                          # 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(108862)
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 = 2,359 (80% power), 3,158 (90% power)
 75% of observed effect: n per arm = 4,108 (80% power), 5,499 (90% power)
 50% of observed effect: n per arm = 9,047 (80% power), 12,111 (90% power)
power.prop.test: 2358.6 
Simulated power at n = 2,359 per arm: 0.799 (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 the sponsor’s own primary analysis as a two-sided Z-test of a mean difference in final values. The reported value is 3, the confidence interval is -2 to 8, the stated confidence level is 95.08%, and p = 0.45. This is the trial’s reported analysis and should be kept distinct from the simple unadjusted recalculation.

The recalculation expresses the comparison as a risk difference for deferred versus immediate ART, based on posted event proportions. It gives an estimate of 0.029, a 95% confidence interval from -0.020 to 0.077, and an unadjusted p-value of 0.247. Differences in the stated measure and method mean these numbers are not direct substitutes for each other. The registry record does not provide enough detail to reconcile them fully or establish that they estimate precisely the same quantity.

Both the sponsor-reported interval and the recalculated interval include zero, so neither summary precisely distinguishes a difference from no difference. The sponsor analysis is not a confirmation that the endpoint label and posted proportions have the same meaning; that ambiguity remains. The record does not indicate a discrepancy flag for the analyses, but the statistical summaries still need to be described according to their separate methods.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a plan for controlling multiplicity across the primary and secondary outcomes. Multiplicity arises when several hypotheses are tested: even if each test is conducted at a conventional error rate, the chance of at least one false-positive result across the set can be greater than for a single test. In general, a prespecified hierarchy or adjustment procedure can help control that risk. No such procedure is described in the record, so unadjusted secondary p-values should be treated as exploratory rather than as a collection of definitive findings.

The record names the primary analysis population as intent-to-treat, with changes from randomized strategy ignored. It also says randomized participants were followed for 48 weeks whether or not ART began as scheduled or at all, and regardless of whether tuberculosis treatment was discontinued. This is useful information about the intended comparison. However, the record does not report the number or reasons for missing outcome observations, the censoring rules, or how missing data were handled beyond identifying Kaplan-Meier estimation for the primary outcome.

In general, Kaplan-Meier methods can accommodate incomplete follow-up by treating participants as censored at their last observed time, but interpretation depends on the censoring process and assumptions. The registry does not report enough information to assess those assumptions or reconstruct the survival estimates. It also does not describe sensitivity analyses for missing outcomes.

The original statistical analysis plan, interim analyses, and sample-size justification are not reported in the registry record. The planning illustrations based on observed effects do not establish what was planned before the trial. These omissions limit assessment of prespecification, selective reporting, and the intended handling of multiple outcomes. They do not invalidate the posted results, but they constrain how confidently the analyses can be interpreted.

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: pulmonary tuberculosis (1.7%), death (1.5%), anaemia (1.5%), hepatotoxicity (1.2%), neutrophil count decreased (1.0%).

The registry reports serious adverse events for 55 of 405 participants in the immediate ART group and 44 of 401 participants in the deferred ART group. It also reports other adverse events for 391 of 405 and 389 of 401 participants, respectively. These are counts of participants reported with events, not a comparison adjusted for follow-up time or other factors. The record does not provide a statistical comparison for these safety summaries in the posted information.

The listed serious-event terms include pulmonary tuberculosis at 1.7%, death at 1.5%, anaemia at 1.5%, hepatotoxicity at 1.2%, neutrophil count decreased at 1.0%, and neutropenia at 0.7%. Those terms are listed without arm-specific percentages in the record. The death entry among serious-event terms should not be confused with the separate deaths field, which is not reported for either group.

These summaries describe reported events, but they do not establish whether an event was caused by a treatment strategy. The registry record does not provide enough detail about event timing, exposure, severity grading by arm, or causal assessment to support stronger comparative safety conclusions.

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

The posted results describe a randomized comparison of two ART-start strategies during tuberculosis treatment, with the primary outcome assessed through week 48. The arm-level primary values are 13% and 16%; the recalculated risk difference for deferred versus immediate ART is 0.029, with a 95% confidence interval that includes zero. The sponsor’s reported analysis also has a confidence interval that includes zero and reports p = 0.45. Taken together, these summaries do not provide a precise estimate of a difference between the strategies.

This does not establish that the strategies are equivalent. A failure to distinguish a difference from zero is not proof that any difference is absent; the interval remains compatible with more than one possibility. Nor do the results demonstrate that the study’s stated hypothesis of a reduction by at least 40% was met. That hypothesis is a planned expectation, not a finding.

The registry’s endpoint wording and percentages create a further limitation: the outcome is called survival without AIDS progression, while the posted proportions and event counts appear difficult to align with that description. Without clarification, the direction of the reported numerical difference should not be translated into a claim that one strategy produced more or less survival without progression.

The secondary outcomes and safety summaries add descriptive information, but they are not a substitute for a clearly defined primary result. The registry does not report multiplicity procedures or detailed missing-data methods. These limits matter when assessing the strength and generality of the evidence. The results describe what was posted for this study and do not, on their own, support medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial addresses a statistical challenge common in clinical research: comparing treatment strategies that differ in timing while participants may not follow the assigned schedule exactly. The registry’s intent-to-treat description focuses the primary comparison on assignment to immediate or deferred ART, rather than selectively comparing only participants who began treatment at the planned time. That distinction is important because adherence after randomization can be related to participant circumstances and outcomes.

The endpoint also combines survival and AIDS progression over follow-up. The registry identifies Kaplan-Meier estimation, a method suited to time-to-event information and incomplete observation under assumptions about censoring. Understanding the method and its assumptions matters because a simple percentage comparison may not convey how event timing and follow-up contribute to an estimate.

At the same time, the record illustrates why careful endpoint definition is essential. A numerical estimate can be calculated and presented with a confidence interval, yet remain difficult to interpret if its values do not clearly correspond to the endpoint’s wording. Statistical precision cannot compensate for uncertainty about what is being estimated.

Finally, the posted primary comparison and sponsor analysis show why estimates, confidence intervals, and study plans should be read together. The intervals include zero, the recalculation is unadjusted, and the record does not report multiplicity or detailed missing-data procedures. These features do not make the results unusable; they define the limits of what can be concluded from them. The distinction between a reported finding, a planning hypothesis, and a planning illustration is central to sound interpretation.

19. Limitations

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

The primary outcome has a notable reporting ambiguity: the registry calls it the percent surviving without AIDS progression, but the displayed percentages and event proportions do not straightforwardly match that wording. The record does not explain whether the values represent the complement of the named outcome, a differently coded endpoint, or another convention. This limits directional interpretation of the comparison.

The registry describes Kaplan-Meier estimation but does not report event times, censoring details, numbers censored, or the assumptions used to handle incomplete follow-up. It states that participants were followed regardless of treatment initiation and tuberculosis-treatment discontinuation, but does not provide enough information to assess completeness of follow-up or the effect of missing observations.

The sponsor’s reported Z-test is labeled as a mean difference in final values, whereas the recalculation is an unadjusted risk difference based on binary event proportions. The record does not fully reconcile the measures or methods. This makes it important to keep them distinct rather than treating the recalculation as a reproduction of the sponsor’s analysis.

Details of the original sample-size rationale, interim analyses, statistical analysis plan, and multiplicity procedures are not reported. The secondary outcomes therefore cannot be assumed to have been adjusted for multiple testing. The registry record also does not provide enough safety detail to assess event timing or treatment attribution. These limitations constrain interpretation of this record; they do not by themselves establish that the trial was conducted improperly.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Immediate Versus Deferred Start of Anti-HIV Therapy in HIV-Infected Adults Being Treated for Tuberculosis — NCT00108862.
• Registry record last updated 2018-10-11; status last verified 2018-09.
• Results first posted 2011-11-02.
• 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, unmasked, parallel-group phase 4 study comparing immediate ART after approximately 2 weeks of tuberculosis treatment with deferred ART after 8 to 12 weeks. The primary endpoint was assessed through week 48 in an intent-to-treat population, and the registry names Kaplan-Meier estimation.

The posted primary values are 13% for immediate ART and 16% for deferred ART. The recalculated risk difference is 0.029, with a 95% confidence interval from -0.020 to 0.077 and p = 0.247. The sponsor-reported mean difference is 3, with a confidence interval from -2 to 8 and p = 0.45. Both comparisons are uncertain, and the endpoint label does not clearly align with the posted proportions.

The record does not report the original sample-size justification, detailed missing-data procedures, interim analyses, or multiplicity plan. Secondary and safety outcomes provide additional descriptive information but warrant cautious interpretation.