Daily Isoniazid to Prevent Tuberculosis in Infants Born to Mothers With HIV: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Daily Isoniazid to Prevent Tuberculosis in Infants Born to Mothers With HIV (NCT00080119), a randomized phase 2, phase 3 study. The primary outcome is Time to Development of Tuberculosis (TB) Disease or Death Among HIV-infected Children.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, placebo-controlled trial with triple masking and phase 2 and phase 3 designations. It records enrollment of 1,354 participants and a terminated status. The reason for termination is not reported in the registry record; the status alone does not establish why the trial ended or what consequences that had for the analysis.

The primary comparison is between HIV-infected children assigned to isoniazid and HIV-infected children assigned to isoniazid placebo. The registry reports 273 participants in the HIVpos/INH group and 274 in the HIVpos/PL group for this endpoint. The two groups also received trimethoprim/sulfamethoxazole as described in the registry’s arm information. For the HIV-infected children, the registry describes daily isoniazid or placebo for 96 weeks and trimethoprim/sulfamethoxazole through one year of age, with possible continuation according to WHO guidelines.

The trial also included perinatally exposed children who were HIV-uninfected, assigned to isoniazid or placebo. Their treatment descriptions differ in the stated duration of trimethoprim/sulfamethoxazole. These children contribute to separate secondary questions, not to the primary population described in the primary endpoint.

Randomization is intended to create comparable groups at allocation, while masking can reduce the influence of treatment knowledge on participant care, assessment, and reporting. The registry labels the masking as triple but does not identify which groups of people were masked. Details of the randomization procedure, allocation concealment, and the trial’s original sample-size justification are not reported in the registry record.

The record lists a start in 2004-02 and primary completion in 2009-05. It does not give a reason for termination or explain whether the termination affected recruitment, follow-up, or the planned analysis. Those details should not be inferred from the status label.

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: Infants perinatally exposed to HIV 91-120 days with documented receipt of Bacille Calmette-Guerin (BCG) vaccine by 30 days (\>=90 days since receipt), no previous diagnosis or treatment of TB or contact with known TB case, stratified by HIV and randomized to receive blinded INH or INH placebo. 3 participants randomized but did not start treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Includes HIVpos who started study treatment. Time from randomization to TB disease/death was calculated. Participants lost-to-follow-up (LTF) \<96 wks (+12wks) censored at the time of LTF. Participants in follow-up at 96 wks free of TB disease censored at 96 wks. Participants on study when study discontinued censored at discontinuation visit.

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 Time to Development of Tuberculosis (TB) Disease or Death Among HIV-infected Children, measured over Through to week 96.

The primary endpoint is time from randomization to the first recorded occurrence of tuberculosis disease or death among HIV-infected children who started study treatment. The registry reports the outcome through week 96 as the percentage reaching tuberculosis disease or death, calculated using the Kaplan–Meier method. It describes diagnostic categories for tuberculosis disease and says endpoint records were reviewed by an Endpoint Review Group.

Combining disease and death creates a single event outcome for the primary comparison. This can address whether the time-to-event experience differs for the combined outcome, but it does not reveal whether any observed difference is attributable to tuberculosis disease, death, or both. The registry does not report separate primary estimates for those components.

A time-to-event endpoint uses information about when an event occurs, rather than only whether it occurred by a fixed point. This is useful when participants have different lengths of follow-up or when some are not observed through the full period. The registry description says participants lost to follow-up before week 96 were censored at the time of loss, while participants still followed and free of tuberculosis disease at week 96 were censored at week 96. The account of censoring is truncated after a further reference to participants still on study, so additional details of endpoint handling are not reported in the registry record.

The endpoint’s interpretation depends on the event definition, follow-up, and censoring assumptions as well as the statistical comparison. It should be read as a result for the combined tuberculosis disease-or-death endpoint in the specified HIV-infected analysis population, not as a direct estimate for every outcome or population in the trial.

7. Results Posted in the Registry

• HIVpos/PL: 28.8% (79/274) versus 27.5% (75/273) on control; risk difference 1.4 percentage points (95% CI -6.2 to 8.9), risk ratio 1.05 (0.80–1.37); unadjusted two-proportion z-test p = 0.724.

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.

Time From Randomization to Development of TB Infection or Death Among HIV-infected Children

• 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:
  • HIVpos/PL: 32.8% (90/274) versus 29.3% (80/273) on control; risk difference 3.5 percentage points (95% CI -4.2 to 11.3), risk ratio 1.12 (0.87–1.44); unadjusted two-proportion z-test p = 0.371.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HIVpos/PL and the control. The interval gives the range of effects that remain compatible with the data.

Time From Randomization to HIV Disease Progression or Death Among HIV-infected Children

• 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:
  • HIVpos/PL: 22.6% (62/274) versus 30.8% (84/273) on control; risk difference -8.1 percentage points (95% CI -15.5 to -0.8), risk ratio 0.74 (0.55–0.98); unadjusted two-proportion z-test p = 0.031.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for HIVpos/PL than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time From Randomization to Development of TB Disease or Death Among Perinatally Exposed, HIV-uninfected Children

• 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:
  • HIVneg/PL: 9.0% (36/401) versus 8.2% (33/403) on control; risk difference 0.8 percentage points (95% CI -3.1 to 4.7), risk ratio 1.10 (0.70–1.72); unadjusted two-proportion z-test p = 0.690.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HIVneg/PL and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several distinct questions: tuberculosis infection, HIV disease progression, tuberculosis disease, death, and adverse events, in HIV-infected children and in perinatally exposed HIV-uninfected children. The posted results therefore broaden the set of outcomes and populations considered, but they do not all measure the same clinical event as the primary endpoint.

Across the secondary results with numerical comparisons posted, the pattern is not uniform. Some estimates are close to no apparent difference, while one comparison has a nominal unadjusted p-value below 0.05. That variation is not, by itself, evidence of a consistent treatment effect across endpoints. The primary result concerns tuberculosis disease or death among HIV-infected children; secondary outcomes may use another event definition or population and should be interpreted on their own terms.

Numerical results for the other listed secondary outcome topics are not reported in the registry record. The record lists seven secondary outcomes, but the registry information available for this account includes numerical comparisons for only some of them. Missing numerical results should not be interpreted as showing no events or no difference.

Secondary analyses generally carry less weight when many outcomes are tested without a reported multiplicity strategy. In general, testing multiple hypotheses increases the chance that at least one result appears notable by chance. The registry does not report a correction for multiple comparisons or a prespecified hierarchy for the secondary tests. Accordingly, unadjusted secondary findings are best read as exploratory signals, not as definitive confirmation or contradiction of the primary analysis.

The secondary results also cannot resolve uncertainty in the primary endpoint. They involve different event definitions and, in some cases, different populations. Their contribution is descriptive: they show how the posted findings extend beyond the primary question, while leaving the primary time-to-event comparison as the principal result for this population and outcome.

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

• Time From Randomization to Development of TB Infection or Death Among HIV-infected Children
• Time From Randomization to HIV Disease Progression or Death Among HIV-infected Children
• Time From Randomization to Development of TB Disease or Death Among Perinatally Exposed, HIV-uninfected Children
• Time From Randomization to Development of TB Disease Among HIV Infected and Perinatally Exposed, HIV-uninfected Children
• Time From Randomization to Development of TB Infection Among HIV-infected and Perinatally Exposed, HIV-uninfected Children
• Time From Randomization to Death Among HIV-infected and Perinatally Exposed, HIV-uninfected Children
• Time From Randomization to First New Grade 3 or Worse Adverse Event Among HIV-infected and Perinatally Exposed, HIV-uninfected Children

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s primary result is a time-to-event analysis. Each participant contributes information from randomization until the endpoint occurs or follow-up ends. The event is the first occurrence of tuberculosis disease or death. The registry reports the percentage reaching that combined endpoint through week 96 using the Kaplan–Meier method, and identifies the sponsor’s comparison method as the log-rank test with a hazard ratio as the effect measure.

What does censoring mean?

In general, censoring means that the exact event time is not observed during the available follow-up, even though the participant’s observed time still contributes information up to a point. The registry says participants lost to follow-up before week 96 were censored at loss, and those still followed and free of tuberculosis disease at week 96 were censored at week 96. The registry’s endpoint description is cut off after mentioning participants still on study, so the complete handling of that situation is not reported in the registry record.

Kaplan–Meier estimation uses the observed event and censoring times to estimate the event experience over follow-up. Its interpretation relies on censoring being handled appropriately; in general, informative loss to follow-up can affect estimates if participants who leave differ in relevant ways from those who remain. The registry does not report an assessment of that assumption. The time-to-event approach is distinct from simply dividing the number of events by the number randomized because it uses event timing and follow-up information.

How should the hazard ratio be read?

In general, a hazard ratio compares the instantaneous event rates between groups over follow-up, subject to the model and comparison assumptions. A value of 1 indicates equal hazards in the comparison; values on either side indicate different relative hazards. The sponsor reports a hazard ratio of 0.98 and a 95% confidence interval from 0.67 to 1.44. Since the interval includes 1, the reported result does not clearly distinguish the groups on this relative time-to-event scale. A hazard ratio is not the same quantity as a difference in the percentage reaching the endpoint by week 96.

The log-rank test is a general method for comparing time-to-event patterns between groups. Its p-value, reported as 0.93, describes how compatible the observed comparison is with a null hypothesis of no difference under the test’s assumptions. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of a difference.

What is the unadjusted recalculation?

The registry also posts group event counts and percentages. A simple unadjusted recalculation compares the posted event proportions without accounting for event timing. For the primary outcome, that recalculation has p = 0.724, with a confidence interval for the risk difference that crosses zero. This check answers a different statistical question from the log-rank analysis. Because the sponsor’s own analysis is the time-to-event analysis reported in the registry, it is the primary analysis to use when describing the sponsor’s result; the unadjusted calculation is supplementary.

In general, a risk difference expresses the contrast in event proportions between groups, whereas a risk ratio or odds ratio expresses a relative contrast. These measures can differ in interpretation and magnitude, and they do not use the event-time information captured by a survival analysis. A confidence interval around any such estimate conveys uncertainty in that particular measure, under its calculation assumptions.

Why do analysis populations matter?

The registry states that the primary analysis includes HIV-infected children who started study treatment. That is narrower than the full enrollment and is not interchangeable with an analysis of every randomized participant. The record does not report a full accounting of exclusions from the primary analysis or a detailed intention-to-treat analysis description. In general, the analysis population should be considered when judging what group the estimate represents and whether departures from randomization could affect comparability.

There are multiple secondary outcomes, and the registry lists seven secondary outcome topics. In general, testing many outcomes creates more opportunities for apparently notable results to arise by chance. An unadjusted secondary p-value does not account for that multiplicity unless a correction or prespecified testing strategy is applied. Such a strategy is not reported in the registry record, so secondary findings should be treated as exploratory rather than as independent confirmation of the primary result.

The registry record does not report the trial’s original sample-size justification, detailed statistical analysis plan, or whether interim analyses were conducted. General explanations of the statistical methods do not fill those record-specific gaps. The planning illustrations based on observed effects are not the original design calculation and do not establish what the trial was designed to detect.

11. Confidence Intervals and Precision

The sponsor’s primary time-to-event estimate is a hazard ratio of 0.98, with a 95% confidence interval from 0.67 to 1.44. In general, a confidence interval gives a range of estimates compatible with the observed data and the method’s assumptions. It is not a guarantee that the true effect lies within that particular interval, and it is not a probability statement about the effect after the data have been observed.

The primary interval includes 1, the value corresponding to equal hazards. It also includes values on both sides of 1, so the posted estimate does not pin down a single direction or a narrow range of relative effects. The point estimate alone is not enough to characterize precision; the interval shows that substantial uncertainty remains around the relative comparison.

The recalculated unadjusted risk-difference interval also crosses zero. Zero is the value corresponding to no difference in event proportions on that scale. The interval therefore does not clearly separate the groups for that unadjusted comparison. Its exact endpoints are not repeated in prose because they are reported with more than three decimal places in the registry-derived calculation.

The two intervals address different estimands: one concerns the time-to-event hazard comparison, while the other concerns a difference in event proportions. They should not be treated as interchangeable. The Kaplan–Meier percentages through week 96 provide an absolute description of the combined outcome, while the hazard ratio summarizes the relative time-to-event comparison.

Precision is also affected by how many endpoint events occur and how follow-up and censoring are distributed. The primary group sizes are reported, but the registry does not provide all details needed to independently assess the effects of follow-up completeness or the censoring assumptions. The confidence interval is therefore an important part of interpretation, but not a substitute for those design and data-quality details.

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 justification. For percentage-outcome comparisons, the figures are participants per arm. Where a planning calculation is explicitly a time-to-event calculation, the figures are 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; each scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of participants per arm, or total events for a time-to-event calculation, associated with an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% column gives the corresponding requirement for a 90% chance. These are design-planning quantities, not estimates of how likely the completed trial was to find a result after its data were collected.

The rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller target effects require more participants or events to distinguish them from random variation under the same assumptions. The large variation in the illustrative requirements across effect assumptions reflects how strongly planning needs depend on the effect size chosen.

These calculations are not observed power. They are hypothetical planning illustrations and do not explain why the trial enrolled its actual number of participants. The trial’s original sample-size assumptions and justification are not reported in the registry record. The illustrations also do not incorporate any unreported design features or interim-analysis arrangements.

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 = 0.275; treatment proportion p₁ = 0.288; average p̄ = 0.282.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6360 = 1.2466.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6360 = 0.5352.
4. n = (1.2466 + 0.5352)² / (0.0136)² = 17,175.9, rounded up to 17,176 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 <- 0.274725274725275                          # control proportion
p1 <- 0.288321167883212                          # 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(80119)
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 = 17,176 (80% power), 22,994 (90% power)
 75% of observed effect: n per arm = 30,424 (80% power), 40,728 (90% power)
 50% of observed effect: n per arm = 68,199 (80% power), 91,299 (90% power)
power.prop.test: 17175.9 
Simulated power at n = 17,176 per arm: 0.797 (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 primary comparison as a log-rank analysis with a hazard ratio of 0.98, a 95% confidence interval from 0.67 to 1.44, and p = 0.93. This is the time-to-event analysis and is the sponsor’s own reported analysis for the primary endpoint. It should take precedence over a simple recalculation from the posted event counts when describing the sponsor’s primary statistical result.

The separate recalculation is an unadjusted comparison of event proportions based on the posted group summaries. Its p-value is 0.724, and its risk-difference interval crosses zero. It does not use the timing of events or the censoring information used by the log-rank method. The recalculation is therefore a supplementary check, not an alternative version of the sponsor’s time-to-event estimate.

Both analyses fail to show a clear separation between the groups, but they quantify different contrasts and rely on different information. Agreement in that broad reading does not make the estimates interchangeable. The registry does not report enough detail to reconstruct the sponsor’s analysis independently, including a complete statistical analysis plan or all censoring details.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes spanning tuberculosis infection, tuberculosis disease, HIV disease progression, death, and adverse events. Conducting several statistical tests creates a multiplicity issue: in general, the more hypotheses examined, the greater the opportunity for a seemingly notable result to arise by chance. The registry record does not report a multiplicity adjustment, a prespecified hierarchy among outcomes, or a detailed plan for interpreting secondary tests. The secondary p-values should therefore be read as unadjusted unless the registry explicitly identifies otherwise.

The record does not report whether interim analyses were conducted, whether any stopping boundaries were used, or how any interim testing would have affected the final inference. The trial’s original sample-size justification and full statistical analysis plan are also not reported in the registry record. These omissions limit assessment of whether the final analysis followed an original prespecified plan.

The primary endpoint description identifies an analysis population of HIV-infected children who started study treatment. It also describes censoring for participants lost to follow-up before week 96 and for participants followed to week 96 without tuberculosis disease. The endpoint description is truncated after another reference to participants on study, so complete handling of the remaining circumstances is not reported in the registry record. Details of missing outcome data, reasons for loss to follow-up, and sensitivity analyses are not reported.

In general, censoring can support time-to-event analysis when the censoring process is appropriately handled, but informative loss to follow-up can affect interpretation. The record does not report an evaluation of this assumption. Nor does it provide a full account of how the primary analysis population relates to all randomized participants, including the number and reasons for any exclusions.

The trial status is terminated, but the reason is not reported in the registry record. It is therefore not possible to determine from the status alone whether termination was administrative, safety-related, related to recruitment, or for another reason, or whether it changed the planned analysis. These gaps are relevant context for judging the strength and completeness of the posted results.

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: gastroenteritis (3.3%), death (2.9%), hepatotoxicity (2.2%), pneumonia (2.2%), neutropenia (1.8%).

The registry reports serious adverse events among 403 HIV-uninfected participants in the isoniazid group, with 25 affected, and among 401 HIV-uninfected participants in the placebo group, with 18 affected. Among HIV-infected participants, it reports 273 at risk and 55 affected in the isoniazid group, and 274 at risk and 42 affected in the placebo group. These are the registry’s serious-event counts and denominators; they do not, by themselves, establish that treatment caused an event or explain differences between groups.

The record also lists serious adverse-event terms with percentages, including gastroenteritis at 3.3%, death at 2.9%, hepatotoxicity at 2.2%, pneumonia at 2.2%, neutropenia at 1.8%, and neutrophil count decreased at 1.5%. These terms describe reported events, not necessarily events judged related to study treatment. The registry does not provide causal attribution in the information used for this account.

Other adverse events are reported separately, with affected counts in each arm, but those counts should not be conflated with the serious-event counts. Death counts in the adverse-event summary are not reported in the registry record. Interpretation of safety would also require context about event definitions, follow-up, severity, and attribution; not all of those details are available in the registry information.

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

The posted primary result describes a comparison of time to tuberculosis disease or death through week 96 among HIV-infected children who started study treatment. The sponsor-reported hazard ratio is 0.98, with a 95% confidence interval from 0.67 to 1.44 and p = 0.93. The result does not provide clear statistical evidence of a difference between the assigned groups on the primary time-to-event endpoint.

That conclusion is not the same as proving the groups are identical. The confidence interval includes 1 and is broad enough to remain compatible with relative effects in either direction. The absence of a statistically clear difference is not proof of no effect, and the point estimate should not be interpreted as a precise estimate of equivalence.

The primary endpoint combines tuberculosis disease and death. It does not reveal which component contributed to the observed outcome, and the registry does not report separate primary analyses for those components. The result also applies to the specified HIV-infected analysis population, not automatically to HIV-uninfected children, all enrolled participants, or other populations.

The registry’s secondary results address other endpoints and populations and do not replace the primary comparison. Their unadjusted nature and the absence of a reported multiplicity strategy warrant caution. Safety counts are descriptive and do not establish whether an event was caused by treatment.

The registry lists the trial as terminated, but does not report the reason or the impact on the planned analysis. It also does not report the original sample-size justification, complete analysis plan, or whether interim analyses occurred. These limitations make it important to distinguish what the posted data show from what cannot be established from the registry record. The results describe this trial’s outcomes and analysis; they do not, by themselves, answer every question about treatment effects or safety.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint and analysis method matters in clinical research. The primary outcome is a time-to-event composite of tuberculosis disease or death, and the sponsor’s log-rank analysis uses event timing and censoring. A simple comparison of event percentages uses a different summary and answers a different statistical question. Both can describe the data, but they are not interchangeable.

The record also illustrates the role of precision. A point estimate can appear close to no difference while its confidence interval still spans a range of relative effects. Reporting the interval alongside the p-value helps distinguish a lack of clear statistical evidence from evidence that the groups are equivalent.

Population definition is another important issue. The primary analysis concerns HIV-infected children who started study treatment, whereas the trial also included perinatally exposed children who were HIV-uninfected. Results from one group cannot be assumed to describe the other. Composite outcomes and multiple secondary endpoints also need careful interpretation because they combine different events or test additional questions.

Finally, the registry record shows why analysis-plan and follow-up details matter. The reason for termination, original sample-size justification, interim-analysis information, complete missing-data handling, and multiplicity strategy are not reported. These details affect how readers assess the connection between the design, the observed data, and the final claims. Clear distinction between sponsor-reported analyses, unadjusted recalculations, and planning illustrations helps prevent those different forms of evidence from being conflated.

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 registry record leaves several trial-specific uncertainties. It labels the study terminated but does not report why, or whether termination changed recruitment, follow-up, or analysis. The record gives enrollment but does not provide the original sample-size justification, so the relation between actual enrollment and the intended statistical precision cannot be assessed from the registry information.

The primary endpoint description specifies the analysis population and some censoring rules, but its text is truncated after another reference to participants on study. The record does not provide a complete account of missing outcomes, reasons for loss to follow-up, or sensitivity analyses. It also does not report an assessment of whether censoring could be related to prognosis.

The sponsor’s reported time-to-event analysis is identified as a log-rank test with a hazard ratio, but the full statistical analysis plan is not reported. Details of the randomization and masking procedures are also absent. The registry calls masking triple but does not identify which roles were masked.

The primary endpoint combines tuberculosis disease and death, without separate primary estimates for each component. The secondary outcomes address other endpoints and populations, but numerical results for all listed secondary outcomes are not reported in the registry record. A multiplicity approach is not described, which limits interpretation of unadjusted secondary findings.

Safety information includes serious-event counts and selected event terms, but the registry information does not establish treatment attribution. Death counts in the adverse-event summary are not reported in the registry record. These limits mean that the posted results support a focused reading of the recorded comparisons, rather than a complete reconstruction of all trial conduct and analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Daily Isoniazid to Prevent Tuberculosis in Infants Born to Mothers With HIV — NCT00080119.
• Registry record last updated 2019-02-05; status last verified 2019-01.
• Results first posted 2010-10-19.
• 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 randomized, triple-masked, parallel-group, placebo-controlled phase 2 and phase 3 trial with enrollment of 1,354 participants and terminated status. The primary comparison concerns HIV-infected children who started study treatment and measures time to tuberculosis disease or death through week 96.

The sponsor-reported log-rank result is a hazard ratio of 0.98, with a 95% confidence interval from 0.67 to 1.44 and p = 0.93. The registry also posts Kaplan–Meier endpoint estimates of 27.4% for the isoniazid group and 28.9% for the placebo group. The record lists secondary outcomes and adverse-event information, but does not report the reason for termination, the original sample-size justification, or a complete statistical analysis plan.