Evaluating the Safety of Immediate Versus Deferred Isoniazid Preventive Therapy Among HIV-Infected Pregnant Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluating the Safety of Immediate Versus Deferred Isoniazid Preventive Therapy Among HIV-Infected Pregnant Women (NCT01494038), a randomized phase 4 study. The primary outcome is Incidence Rate of Combined Endpoint: Grade 3 or Higher Adverse Events (AEs) Related to Treatment, or AE Causing Discontinuation of Treatment.

2. Clinical Question

The trial addressed the timing of preventive therapy, rather than a comparison of isoniazid with no treatment over the entire follow-up period: both groups were scheduled to receive isoniazid, but at different stages relative to pregnancy and postpartum. The primary endpoint combined serious treatment-related adverse events with events that caused permanent discontinuation, so it captured both a specified severity threshold and a treatment-limiting outcome. The registry record also lists pregnancy and infant outcomes, including fetal death, premature birth, low birth weight, congenital anomaly, and infant adverse events. Those outcomes provide additional context, but they are distinct from the primary safety question.

3. Trial Design

This was a Phase IV randomized, double-blind, placebo-controlled, parallel-group trial. The registry record reports enrollment of 956 women and a completed trial. The recorded start date was 2014-08-19, and the primary completion date was 2017-09-06. The sponsor was the National Institute of Allergy and Infectious Diseases (NIAID).

Random assignment placed participants into one of two treatment-timing groups. In the immediate group, isoniazid began at study entry during pregnancy and was followed by placebo beginning after Week 28 through Week 40 postpartum. In the deferred group, placebo was used from study entry through Week 12 postpartum, followed by isoniazid through Week 40 postpartum. The placebo and double-blind features were intended to make the assigned schedules less apparent to participants and trial personnel; the specific procedures used to maintain masking are not reported in the registry record.

The primary endpoint was an incidence rate, not simply a count of women with at least one event. The registry describes a Mantel-Haenszel weighted rate calculation using gestational-age-at-entry strata: less than 24 weeks or greater than or equal to 24 weeks. The primary endpoint population is described as all women enrolled. The primary follow-up period ran from study entry through Week 48 after birth.

The record lists 39 outcome measures and 33 analyses. The trial's original sample-size justification, planned interim analyses, detailed allocation procedures, and the full statistical analysis plan are not reported in the registry record. The posted analysis information should therefore be read as the record of reported results, not as a complete account of every design and analysis decision.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All women enrolled.

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.

Population: All women in study.

6. Primary Endpoint

The registry lists the primary outcome as Incidence Rate of Combined Endpoint: Grade 3 or Higher Adverse Events (AEs) Related to Treatment, or AE Causing Discontinuation of Treatment, measured over Measured from study entry through Week 48 after birth.

The primary endpoint is the incidence rate of the combined outcome of Grade 3 or higher adverse events judged related to isoniazid or its placebo, or an adverse event causing permanent discontinuation of study treatment. Events could include laboratory results, signs or symptoms, or diagnoses. An independent endpoint review committee judged whether events were possibly, probably, or definitely related to the assigned study treatment. Severity was graded using Division of AIDS criteria or protocol-defined hepatotoxicity measures.

The endpoint was measured from study entry through Week 48 after birth and expressed as events per 100 person-years. An incidence rate accounts for the amount of follow-up time contributed by participants, unlike a simple proportion that counts participants with an event without incorporating their time at risk. This can be useful when participants contribute different amounts of observation time or when the analysis is framed around the rate at which events occur during follow-up. That is a general statistical explanation; the registry record does not report how much follow-up time each participant contributed.

Combining severe treatment-related events with events that led to permanent discontinuation focuses the endpoint on outcomes that were considered clinically consequential for safety monitoring or treatment continuation. At the same time, a composite endpoint combines different event types. Its overall rate does not reveal, by itself, how much each component contributed or whether the components followed the same pattern. Component-specific primary results are not reported in the registry record.

7. Results Posted in the Registry

• Arm B (Deferred INH Treatment): 14.93 versus 15.03 (events per 100 person-years) on control; rate ratio 0.99 (95% CI 0.71–1.40, approximate, Poisson model); p ≈ 0.969.

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.

Number of Mothers With a Fetal Death

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B (Deferred INH Treatment): 1.9% (9/466) versus 3.7% (17/459) on control; risk difference -1.8 percentage points (95% CI -3.9 to 0.4), risk ratio 0.52 (0.23–1.16); unadjusted two-proportion z-test p = 0.103.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Deferred INH Treatment) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Mothers With an Infant Born Prematurely

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B (Deferred INH Treatment): 8.7% (40/458) versus 10.9% (48/442) on control; risk difference -2.1 percentage points (95% CI -6.0 to 1.8), risk ratio 0.80 (0.54–1.20); unadjusted two-proportion z-test p = 0.283.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Deferred INH Treatment) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Infants With Grade 3 or Higher Clinical or Laboratory AE

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B (Deferred INH Treatment): 42.2% (196/464) versus 43.4% (193/445) on control; risk difference -1.1 percentage points (95% CI -7.6 to 5.3), risk ratio 0.97 (0.84–1.13); unadjusted two-proportion z-test p = 0.731.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Deferred INH Treatment) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the safety and pregnancy context beyond the primary composite. They include maternal pregnancy outcomes and infant adverse events, each with its own definition, follow-up period, and analysis population. The posted numerical comparisons for fetal death, premature birth, and infant Grade 3 or higher adverse events have confidence intervals that include the corresponding no-difference value. This overall pattern does not establish a clear between-group difference for those comparisons, but it does not prove that the groups are equivalent.

These secondary findings are related to the primary question because they describe additional outcomes in the same trial population and treatment schedules. They are not interchangeable with the primary endpoint: pregnancy events, infant events, and the rate of treatment-related maternal events represent different outcomes and may be measured over different periods. The primary result should remain the central comparison for the endpoint designated as primary, with secondary outcomes serving as supporting context rather than as a substitute.

The registry lists 38 posted secondary outcomes. When many outcomes are examined, the chance of obtaining at least one apparently unusual result by chance can increase. General statistical explanation: multiplicity adjustments or a prespecified hierarchy can address some of this issue, but the registry record does not report an adjustment strategy for the secondary analyses. Accordingly, unadjusted secondary results carry less evidential weight than a single prespecified primary analysis, especially when interpreted across a broad set of outcomes.

The record includes sponsor-reported Fisher exact p-values for fetal death and premature birth, but does not list a sponsor-reported analysis for the infant Grade 3 or higher adverse-event outcome. The detailed statistical analysis plan and the intended confirmatory status of the secondary outcomes are not reported in the registry record. The secondary results should therefore be read as descriptive or supportive evidence unless the record indicates otherwise, not as a collection of independent definitive tests.

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

• Number of Mothers With a Fetal Death
• Number of Mothers With a Fetus Small for Gestational Age
• Number of Mothers With an Infant Born Prematurely
• Number of Mothers With a Low Birth-weight Infant
• Number of Mothers With an Infant With a Congenital Anomaly
• Number of Mothers With an Adverse Pregnancy Outcome: Spontaneous Abortion, Stillbirth, Premature Birth, Low Birth Weight, or Congenital Anomaly
• Number of Infants With Grade 3 or Higher Clinical or Laboratory AE
• Number of Infants With Grade 3 or Higher Clinical or Laboratory AE Related to Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is an event rate. General explanation: a rate uses the amount of time participants are observed, whereas a risk or proportion uses participants as the denominator and asks how many experienced an outcome during a defined period. The primary endpoint is reported in events per 100 person-years. Person-time allows follow-up contributions to be reflected in the denominator, but the registry record does not provide participant-level person-time or the details of how censoring was handled.

What does the rate ratio express?

A rate ratio compares one group's event rate with another group's rate. A value of 1 represents equal rates on the ratio scale; values below or above 1 indicate that the numerator rate is lower or higher, respectively, under the chosen ordering. The recalculated estimate compares deferred with immediate treatment and is 0.993. Its 95% confidence interval is 0.706 to 1.398. Because the interval includes 1, the recalculated result is compatible with equal rates as well as with rate differences in either direction. This is a general interpretation of a ratio confidence interval; it does not establish that any particular difference is clinically important.

What does the rate difference express?

A rate difference subtracts one group's rate from another group's rate and remains on the rate scale. The sponsor-reported incidence rate difference is 0.10, with a 95% confidence interval from -4.77 to 4.98. An interval that crosses 0 includes no difference on that scale. Rate differences and rate ratios answer related but distinct questions: a difference describes the absolute separation in rates, while a ratio describes their relative relationship. The sponsor's reported analysis is the registry's stated non-inferiority analysis. The non-inferiority margin is not reported in the registry record, so the confidence interval cannot be judged against that missing criterion.

Why use gestational-age strata?

The registry states that the primary incidence rate was calculated using Mantel-Haenszel weighting across two strata defined by gestational age at study entry: less than 24 weeks and greater than or equal to 24 weeks. General explanation: stratified methods estimate a comparison while accounting for a grouping variable by forming or combining comparisons within its categories. This can help prevent differences in the distribution of that variable from dominating an overall comparison. The registry record does not report stratum-specific event rates, the weights, or the detailed calculation, so those cannot be independently assessed from the posted summary.

The recalculated rate ratio is explicitly unadjusted. It is a simple comparison of the posted arm-level summary rates, not a reproduction of the sponsor's stratified analysis. Its p-value is also unadjusted. The recalculation is useful as a transparent summary-based comparison, but it should not be mistaken for the trial's full analysis or substituted for the sponsor-reported analysis.

How should confidence intervals and p-values be read?

General explanation: a confidence interval expresses the uncertainty associated with an estimate under the method's assumptions. A wider interval indicates less precision than a narrower interval on the same scale. A p-value summarizes how unusual data at least as discrepant as those observed would be under a specified null model; it is not the chance that the null hypothesis is true. These measures answer different questions, so neither should be interpreted in isolation. The registry record does not report all model diagnostics, distributional checks, or analysis-plan details that would be needed for a complete independent assessment.

The recalculated rate comparison uses a Poisson approach, as indicated in the calculation record. General explanation: Poisson methods are commonly used for counts in relation to exposure time. They rely on assumptions about the count process; departures such as over-dispersion, where observed variation exceeds the model's expectation, can affect standard errors and interval coverage. The registry does not report whether over-dispersion was assessed or how it would have been addressed. The sponsor's reported Mantel-Haenszel weighted analysis should be distinguished from this unadjusted recalculation.

For secondary binary outcomes, the recalculated comparisons use risk differences: the difference between the proportions with an outcome in the two groups. The registry also reports Fisher exact tests for fetal death and premature birth, with p-values of 0.093 and 0.288, respectively. A reported Fisher exact method is suitable for testing associations in a two-group binary table without relying on a large-sample approximation for the test, although the registry record does not provide further procedural details. No sponsor-reported analysis is listed for the infant Grade 3 or higher adverse-event outcome.

All these statistics depend on the outcome definitions, populations, follow-up windows, and analysis choices. The primary endpoint has a defined all-enrolled population and follow-up period, while the secondary outcomes have their own denominators and timeframes. General statistical interpretation should preserve those distinctions rather than treating all reported comparisons as if they were the same estimand.

11. Confidence Intervals and Precision

The recalculated primary rate ratio is 0.993, with a 95% confidence interval of 0.706 to 1.398. General explanation: a confidence interval describes uncertainty around an estimate under the method used to calculate it. The interval is not a guarantee that the true value lies within its limits, and it does not assign a probability to each possible value. Its width is a practical indication of how precisely the comparison has been estimated.

For a rate ratio, the no-difference value is 1. The primary interval extends on both sides of 1, so it is compatible with no rate difference as well as with a lower or higher rate in the deferred group. The point estimate is close to 1, but the interval is substantially broader than the point estimate alone might suggest. Thus, a close point estimate should not be read as precise proof of equal rates.

The sponsor-reported incidence rate difference is 0.10, with a 95% confidence interval from -4.77 to 4.98. On the difference scale, 0 is the no-difference value, and this interval includes it. The sponsor analysis is weighted by gestational-age strata according to the registry description; the recalculated ratio is unadjusted. These intervals therefore describe different effect measures and analysis approaches, and should not be compared as if one were a direct restatement of the other.

Precision also depends on the number of events, exposure time, and analytic assumptions, not only the number enrolled. The registry gives the primary arm sizes and rates, but does not report the participant-level exposure distribution or event-time details. The posted interval is the clearest summary of uncertainty available for the recalculated comparison; fuller assessment of its assumptions is not possible from the registry record.

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 illustrations show the number of participants per arm for the binary secondary outcomes and the number of total events for time-to-event outcomes. The primary outcome is an event rate; the planning illustration for it is framed in total events, consistent with the stated convention for time-to-event tables. These figures are not counts observed in the trial. They are calculations based on the observed effect and stated planning assumptions, not the trial's original design justification.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect as the effect to detect. The 80% power column means the illustrated number needed under those assumptions for an 80% chance of detecting that specified effect if it were the true effect and the assumptions held. The 90% power column gives the corresponding illustration for a 90% chance. These are planning concepts, not guarantees about a future study's result.

The scenarios range from planning for 100% of the observed effect to planning for 75% or 50% of that effect. A smaller effect is harder to distinguish from random variation, so detecting a smaller effect generally requires more participants or events. That pattern is reflected in the increasing planning figures as the assumed effect becomes a smaller fraction of the observed effect. The primary estimate is close to the no-difference value, so using the observed effect as a target yields very large illustrations; these calculations should not be mistaken for a practical recommendation about a future trial.

The illustrations are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after results are known. The original sample-size assumptions and justification for this trial are not reported in the registry record, so the planning figures do not explain why the trial enrolled the number of participants it did.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.1503; treatment rate λ₁ = 0.1493 events per patient-year; follow-up T = 0.92 years.
2. n = (1.96 + 0.842)² × (1/0.1503 + 1/0.1493) / (0.92 × [ln(0.993)]²) = 2,556,312.4, rounded up to 2,556,313 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
lambda0 <- 0.1503                      # control rate, events per patient-year
lambda1 <- 0.1493                      # treatment rate
tt      <- 0.919892679187428                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(1494038)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 2,556,313 (80% power), 3,422,178 (90% power)
 75% of observed effect: n per arm = 4,540,754 (80% power), 6,078,781 (90% power)
 50% of observed effect: n per arm = 10,208,157 (80% power), 13,665,826 (90% power)
Simulated power, Poisson counts, n = 2,556,313 per arm: 0.793
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.626

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis of incidence rate difference: 0.10, with a 95% confidence interval from -4.77 to 4.98, identified as a non-inferiority analysis. The primary outcome description says the incidence rate was calculated by Mantel-Haenszel weighting across gestational-age-at-entry strata. The registry does not report the non-inferiority margin or the complete decision rule used for that analysis.

The recalculated summary comparison uses the posted arm-level rates to estimate an unadjusted rate ratio of 0.993, with a 95% confidence interval of 0.706 to 1.398 and an unadjusted p-value of 0.969. This calculation is not the sponsor's weighted rate-difference analysis. The measures are on different scales, and the recalculation does not incorporate the documented gestational-age weighting. The recalculated p-value is not a sponsor-reported p-value for the non-inferiority analysis.

Because these approaches answer related but not identical statistical questions, the sponsor's reported result should be read as its own analysis rather than replaced by the unadjusted recalculation. The recalculation offers a separate summary-based perspective, with its limitations made explicit. The registry record does not flag a discrepancy between the posted analyses, but it also does not provide enough detail to independently reconstruct the sponsor's non-inferiority procedure or assess it against a prespecified margin.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a large set of outcomes and analyses: 39 outcome measures, 33 analyses, and 38 posted secondary outcomes. Testing many outcomes can increase the likelihood that at least one comparison appears statistically notable by chance, even when no underlying difference exists. General statistical explanation: multiplicity procedures can control a specified error rate across a family of tests, while a prespecified hierarchy can allocate interpretive priority among outcomes. The registry record does not report whether a multiplicity adjustment, hierarchical testing strategy, or other familywise error approach was used for the secondary outcomes.

The primary endpoint is identified, and its comparison is described as a Mantel-Haenszel weighted incidence rate analysis across gestational-age strata. However, the full analysis plan, the planned handling of secondary comparisons, and details of any interim analyses are not reported in the registry record. It is therefore not possible to determine from the record whether every analysis was prespecified, whether any outcomes or analyses were added after trial initiation, or how the overall set of tests was intended to be interpreted.

The primary endpoint population is stated as all women enrolled. The registry gives arm-specific denominators for the primary rate and for the posted secondary outcomes, but does not explain why the secondary denominators differ or how missing observations were handled. The reasons for unavailable outcome data, exclusions from individual analyses, and any imputation or sensitivity analyses are not reported in the registry record. A smaller outcome denominator should not automatically be interpreted as missingness or as a specific exclusion process without those details.

Definitions of missingness, censoring, and analysis populations matter because they can affect both the estimate and its uncertainty. General statistical explanation: if participants with unavailable outcomes differ systematically from those with observed outcomes, a complete-case comparison can be biased; sensitivity analyses can explore how conclusions might change under alternative assumptions. The registry record does not report such sensitivity analyses or enough information to assess the potential impact of unavailable data.

These gaps limit a full evaluation of the inferential framework, but they do not erase the posted estimates. They mean that secondary p-values and confidence intervals should be interpreted with caution and that the results cannot be treated as a complete account of the planned analysis strategy.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

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: sepsis neonatal (3.4%), premature baby (2.6%), foetal death (2.5%), pneumonia (2.2%), pre-eclampsia (1.7%).

The registry lists serious adverse events for mothers and infants separately by assigned treatment timing. Among mothers, 71 of 477 in the immediate group and 69 of 479 in the deferred group were recorded as affected by a serious adverse event. The corresponding infant counts were 86 of 445 and 91 of 464. These are counts of participants affected, not rates per person-time, and they are not the primary endpoint's treatment-related composite.

The record also lists other adverse events: 438 of 477 mothers in the immediate group and 449 of 479 mothers in the deferred group; for infants, 417 of 445 and 430 of 464. Death counts are listed as 2 and 4 among mothers, and 11 and 17 among infants, for the immediate and deferred groups respectively. These counts should be read within their recorded group denominators and outcome categories, not as proof of a causal difference between schedules.

The most frequently listed serious event terms include Sepsis neonatal (3.4%), Premature baby (2.6%), Foetal death (2.5%), Pneumonia (2.2%), Pre-eclampsia (1.7%), and Urinary tract infection (1.5%). The registry record does not specify in this summary the denominator used for each listed percentage or provide comparative statistical analyses for these terms. Event counts and term frequencies describe what was recorded; they do not, by themselves, establish whether an event was related to treatment.

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

The primary posted rates are 15.03 events per 100 person-years for immediate treatment and 14.93 events per 100 person-years for deferred treatment. The recalculated rate ratio is close to 1, with a 95% confidence interval of 0.706 to 1.398. These results describe similar point estimates, while leaving meaningful uncertainty about the underlying rate relationship. The sponsor-reported rate difference also has a confidence interval that includes 0.

These findings do not prove that the schedules have identical effects. A failure to demonstrate a difference is not the same as demonstrating equivalence. Equivalence and non-inferiority claims require defined margins and appropriate prespecified analyses. Although the registry labels the sponsor's analysis as non-inferiority, its margin and detailed criteria are not reported in the registry record, so that label alone is not enough to independently assess the conclusion.

The primary endpoint combines events judged treatment-related at Grade 3 or higher with events causing permanent discontinuation. It does not cover every possible safety outcome, and the overall rate does not reveal the contribution of each component. Secondary pregnancy and infant outcomes provide additional descriptions but are not substitutes for the primary endpoint. Their interpretation is limited by the number of outcomes considered, their differing denominators, and the absence of reported multiplicity procedures.

The trial compares different timing strategies in a particular population: HIV-infected pregnant women in high tuberculosis incidence settings. The results should be understood within that setting and the study's treatment schedules and follow-up period. The registry record does not report enough detail about missing data, the original design assumptions, or the full analysis plan to resolve every uncertainty about the estimates.

Statistically, the most defensible reading is that the observed primary rates were close, while the uncertainty intervals do not exclude a range of rate relationships. Neither the point estimates nor the p-value should be turned into a general claim about all women, all treatment regimens, or all relevant outcomes. The results describe the posted trial data and analyses, not a universal conclusion.

18. Why This Trial Matters Statistically

This trial illustrates why an estimate and its uncertainty should be read together. The primary rates, 15.03 and 14.93 events per 100 person-years, are close as point estimates, and the recalculated rate ratio is 0.993. Yet its 95% confidence interval of 0.706 to 1.398 allows a range of rate ratios around that estimate. Looking only at the point estimate could make the result seem more definitive than the interval supports.

It also demonstrates that the statistical scale matters. The sponsor reports a rate difference, while the recalculation is a rate ratio. A rate difference expresses absolute separation; a rate ratio expresses a relative comparison. The sponsor's calculation is described as weighted by gestational-age strata, whereas the recalculation is unadjusted. Distinguishing these approaches prevents a summary-based calculation from being mistaken for the trial's own primary analysis.

The non-inferiority label highlights the importance of design information beyond a p-value. Interpreting a non-inferiority result requires the prespecified margin and analysis criteria. Those details are not reported in the registry record. Without them, a reader can describe the sponsor's estimate and interval, but cannot fully evaluate the non-inferiority decision from the registry summary alone.

Finally, the many secondary outcomes show why multiplicity and analysis populations matter. Different outcomes have different denominators and timeframes, and a broad set of unadjusted comparisons can produce results that are easy to overinterpret. Clear outcome definitions, transparent handling of missing data, and a prespecified analysis plan are important for judging how much confidence to place in each result. Where those details are not reported, interpretation should remain proportionate to the information available.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record gives a useful summary of the trial design and posted outcome results, but several details needed for a full statistical appraisal are not reported. The original sample-size justification and assumptions are not reported, so the enrollment target cannot be evaluated against the trial's intended detectable effect or non-inferiority objective. The non-inferiority margin and detailed decision criteria are also not reported.

The primary analysis is described as a Mantel-Haenszel weighted rate calculation across two gestational-age strata, but stratum-specific results, weights, and full implementation details are not reported. The recalculated rate ratio is based on unadjusted summary rates and should not be interpreted as a reconstruction of that weighted analysis. The registry record does not report the full statistical analysis plan, model diagnostics, or whether over-dispersion was assessed.

Reasons for the varying secondary-outcome denominators, methods for handling missing observations, and sensitivity analyses are not reported. Nor are details of planned interim analyses or multiplicity handling. These omissions limit the ability to assess whether the posted analyses match all prespecified plans or how robust the secondary comparisons are to missing data and multiple testing.

The primary endpoint combines treatment-related severe adverse events with events causing permanent discontinuation. Component-specific results are not reported in the registry record, so the combined rate cannot show which component contributed more. The safety summary includes serious and other event counts, but the record does not provide comparative analyses for each listed event term or clarify the denominator for every term percentage in that summary.

Finally, interpretation is limited to the trial population, assigned schedules, endpoint definitions, and follow-up described in the registry. The record does not provide enough information to determine how well the findings apply beyond those conditions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluating the Safety of Immediate Versus Deferred Isoniazid Preventive Therapy Among HIV-Infected Pregnant Women — NCT01494038.
• Registry record last updated 2021-11-05; status last verified 2018-10.
• Results first posted 2018-11-20.
• 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

NCT01494038 is a completed Phase IV randomized, double-blind, placebo-controlled, parallel-group trial of immediate versus deferred isoniazid preventive therapy among HIV-infected pregnant women in high tuberculosis incidence settings. The registry reports enrollment of 956 participants. Immediate treatment began during pregnancy; deferred treatment began postpartum.

The primary outcome was the incidence rate of Grade 3 or higher treatment-related adverse events or adverse events causing permanent treatment discontinuation, measured from study entry through Week 48 after birth. The posted arm rates were 15.03 and 14.93 events per 100 person-years. A recalculated unadjusted rate ratio was 0.993, with a 95% confidence interval of 0.706 to 1.398. The sponsor reported a gestational-age-stratified non-inferiority analysis as an incidence rate difference of 0.10, with a 95% confidence interval from -4.77 to 4.98.

The registry also lists pregnancy and infant outcomes. The non-inferiority margin, full analysis plan, original sample-size justification, multiplicity approach, and detailed missing-data handling are not reported in the registry record.