Pediatric Urgent Start of Highly Active Antiretroviral Treatment (HAART): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pediatric Urgent Start of Highly Active Antiretroviral Treatment (HAART) (NCT02063880), a randomized na study. The primary outcome is All-cause Mortality.

2. Clinical Question

The clinical question concerns timing of ART initiation during hospitalization for a serious infection, rather than a comparison of different ART regimens. The registry record describes possible competing considerations: children might be too ill to benefit from treatment, while urgent treatment could also be associated with immune reconstitution inflammatory syndrome (IRIS), drug toxicity, or interactions. Those statements describe the study's rationale and hypotheses, not conclusions established by the posted results.

The primary outcome is all-cause mortality, and the record also posts participant counts for IRIS and potential drug toxicity. The trial was randomized and unblinded, with parallel treatment arms. Its posted outcome denominators were 90 for urgent ART and 91 for early ART. The registry record does not report a separate analysis population definition or explain how participants with incomplete follow-up were handled.

3. Trial Design

The registry record describes a randomized, unblinded, parallel-group clinical trial in hospitalized children with HIV-1 infection and severe co-infections. Participants were allocated to urgent ART or early ART. Urgent treatment was defined as HAART initiation within 48 hours of enrollment, and early treatment as initiation 7-14 days after enrollment. The brief summary says treatment was to follow World Health Organization and Kenyan national guidelines, while the arm descriptions specifically refer to regimens recommended by the Kenyan Ministry of Health.

The registry record lists an enrollment of 183. The study summary had described a target of 360 children, 180 per arm, so the recorded enrollment is below that stated target. The outcome summaries include 90 participants in the urgent arm and 91 in the early arm. The record does not explain the relationship between the enrollment figure, the outcome denominators, and any participants who may not have contributed to an outcome.

The record lists the trial as completed, with a start date of 2013-03 and a primary completion date of 2015-11. The brief summary anticipated enrollment over 36-48 months and routine follow-up for a maximum of 6 months for each infant; the primary outcome timeframe is stated as 6 months post-HAART initiation. Those planned-duration descriptions should not be treated as evidence that every participant had complete follow-up.

The record identifies all-cause mortality as the primary outcome and lists IRIS and potential drug toxicity as secondary outcomes. It also describes aims to examine co-factors for mortality, IRIS, and drug toxicity, but no analyses of those co-factors are posted. The registry record does not report the original sample-size justification, a detailed analysis plan, interim analyses, or the methods used to preserve allocation concealment. The record says masking was none, so participants and study personnel were not blinded according to the listed design.

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:

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 All-cause Mortality, measured over 6 months post-HAART initiation.

The primary endpoint is the number of participants with all-cause mortality, assessed at 6 months post-HAART initiation. All-cause mortality counts deaths regardless of their attributed cause, providing a direct summary of whether participants died during the stated outcome period. The registry record reports 21 deaths among 90 participants in the urgent ART arm and 18 among 91 participants in the early ART arm.

For a binary outcome such as death occurring or not occurring, an arm-specific risk represents the proportion of participants with the event in that arm. Comparing those risks gives an estimate of the absolute difference between treatment groups. The posted comparison reports the risk difference for early ART relative to urgent ART. A negative value therefore corresponds to a lower observed event proportion in the early ART group in this particular comparison; it is an estimate, not proof that treatment timing caused a difference.

Mortality is used as the primary outcome in the registry record, while IRIS and potential drug toxicity are listed as secondary outcomes. This choice gives the trial a principal comparison focused on deaths rather than on a collection of outcomes with different meanings. The registry record does not provide additional detail on endpoint adjudication, the exact rules used to establish cause or timing of death, or how missing outcome status was handled.

7. Results Posted in the Registry

• Early ART: 19.8% (18/91) versus 23.3% (21/90) on control; risk difference -3.6 percentage points (95% CI -15.5 to 8.4), risk ratio 0.85 (0.49–1.48); unadjusted two-proportion z-test p = 0.561.

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 Participants With Evidence of Immune Reconstitution and Inflammatory Syndrome (IRIS)

• 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:
  • Early ART: 13.2% (12/91) versus 11.1% (10/90) on control; risk difference 2.1 percentage points (95% CI -7.4 to 11.6), risk ratio 1.19 (0.54–2.61); unadjusted two-proportion z-test p = 0.669.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Early ART and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Potential Drug Toxicity

• 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:
  • Early ART: 16.5% (15/91) versus 25.6% (23/90) on control; risk difference -9.1 percentage points (95% CI -20.9 to 2.7), risk ratio 0.65 (0.36–1.15); unadjusted two-proportion z-test p = 0.134.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Early ART and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover IRIS and potential drug toxicity, both assessed over 6 months post-HAART initiation. Their point estimates do not all point in the same direction: the early ART arm has a slightly higher observed IRIS risk, while the posted potential-drug-toxicity risk is lower in that arm. The uncertainty around each comparison is broad, and neither secondary result establishes a clear difference between treatment arms.

This mixed pattern does not conflict with the primary mortality result. The outcomes measure different events, and the primary endpoint is the mortality comparison that the registry identifies as primary. Secondary outcomes can help describe other aspects of the trial, including possible treatment-related harms, but they do not replace the primary comparison or resolve its uncertainty. The record's rationale specifically identifies IRIS and drug toxicity as possible concerns with urgent ART, making their monitoring relevant to the trial question without making them proof of a causal mechanism.

The registry record lists unadjusted p-values for the secondary comparisons but no reported analyses beyond the posted summaries. When several outcomes are examined, the chance of obtaining at least one apparently noteworthy result by chance can increase if no multiplicity strategy is used. The record does not report whether such a strategy was planned. For that reason, secondary p-values should be treated as exploratory evidence unless a prespecified analysis plan establishes otherwise. This does not mean the outcomes are unimportant; it means their inferential weight is limited by the unreported analysis plan and the number of outcomes considered.

There are also limits to what the secondary results can say about safety. The posted measures are participant counts for IRIS and potential drug toxicity, and the registry record does not give definitions, severity grading, timing, or attribution procedures for those endpoints. The results are therefore descriptive summaries of the listed outcomes, not a complete account of every potential adverse effect or of the causal relationship between treatment and an event.

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

• Number of Participants With Evidence of Immune Reconstitution and Inflammatory Syndrome (IRIS)
• Number of Participants With Potential Drug Toxicity

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are participant counts for events, so the primary endpoint is binary: each participant either had a recorded death during the stated outcome period or did not. The registry record reports arm denominators alongside the event counts. For binary outcomes, the arm-specific risk is the event count divided by the number of participants in that arm; the posted record also supplies those risks and comparison statistics. No additional calculations are needed to read the reported comparison.

What does the risk difference mean?

The risk difference expresses the absolute contrast between event risks in the two arms. The primary comparison is presented as early ART relative to urgent ART. Its estimate is -0.035. Under that ordering, a negative estimate means the posted event risk is lower in the early ART arm. The risk difference is useful because it describes the contrast on the risk scale, in the same absolute units as the underlying event probabilities. It does not, by itself, show whether the difference is precise or whether it arose because of treatment timing.

The risk difference is accompanied by a confidence interval from -0.155 to 0.084. A confidence interval describes the range of values reasonably compatible with the data and the statistical method, subject to the method's assumptions. Repeated use of a procedure with the stated coverage would capture the true parameter at that rate in the long run; a particular interval is not a probability statement about the fixed parameter. Since this interval crosses zero, the data are compatible with no absolute difference as well as with differences in either direction.

How do relative measures differ?

The registry record also posts a risk ratio and an odds ratio. A risk ratio compares the risks directly; a value of 1 represents equal risks. The reported risk ratio is 0.848, with a confidence interval from 0.485 to 1.481. An odds ratio compares odds rather than risks, and a value of 1 represents equal odds. The reported odds ratio is 0.810, with a confidence interval from 0.398 to 1.649. Both intervals include their respective no-difference values, so both relative measures also leave substantial uncertainty.

Risk differences, risk ratios, and odds ratios answer related but distinct questions. The absolute difference communicates how far apart the event risks are on the risk scale; the ratios express a relative contrast. The estimates may be numerically different without contradiction because the scales differ. For an outcome that is not rare, an odds ratio should not be read as though it were a risk ratio. The record posts all three forms for the primary comparison, but the registry record does not describe a preferred measure in a detailed statistical analysis plan.

What does the p-value contribute?

The posted p-value for the primary comparison is 0.561 and is labeled unadjusted. A p-value is calculated under a statistical model that assumes a specified null hypothesis, commonly no difference between arms. It measures how unusual data at least as incompatible with that null would be under the model. It is not a measure of effect size, the probability that the result is due to chance, or the probability that the null hypothesis is true. A comparatively large p-value does not establish equivalence; an equivalence conclusion would require a prespecified equivalence margin and an analysis designed for that question. Such a margin is not reported in the registry record.

The p-value and confidence interval are two ways of conveying information from an inferential analysis, but they emphasize different aspects. The interval displays the range and direction of estimates compatible with the data, while the p-value summarizes evidence relative to a null value. Here, the interval's inclusion of zero aligns with the unadjusted p-value not indicating a clear difference under a conventional null-hypothesis test. The record does not report whether the posted p-values use a particular covariate adjustment, although the displayed comparison is an unadjusted comparison of arm summaries.

What is and is not reported about the analysis?

The record identifies random allocation and an unblinded parallel design. Random allocation supports comparisons between assigned groups, while blinding can affect how care, outcome assessment, or reporting occurs. Because the study was unblinded, expectations could potentially influence some aspects of conduct or assessment; the registry record does not describe whether outcome assessment was independently adjudicated. All-cause mortality is less dependent on subjective classification than some outcomes, but the record does not provide endpoint-assessment procedures, so no further assumption about ascertainment is warranted.

No reported analyses are listed for the secondary outcomes, and the record does not post an adjusted or time-to-event analysis for the primary endpoint. It also does not report a statistical analysis plan, treatment of missing data, analysis population, handling of protocol deviations, or a multiplicity procedure. These omissions limit what can be inferred about the prespecified status of tests and about whether the posted results reflect all randomized participants. A statistically significant or nonsignificant label should not be substituted for those missing details.

Finally, the enrollment summary lists 183 participants, while the outcome denominators are 90 and 91. The brief description had stated a planned enrollment of 360, with 180 per arm. The registry record does not explain the target, the shortfall, or the denominator accounting. Those details should be kept separate: the planned target describes what the summary anticipated, the enrollment figure describes the recorded enrollment, and the outcome denominators describe the participants included in the posted endpoint summaries.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.035, with a 95% confidence interval from -0.155 to 0.084. This interval spans zero, so the posted results are compatible with no difference in mortality risk and also with effects favoring either arm. Its width indicates that the estimate is not precise enough to distinguish among these possibilities. The point estimate alone should not be treated as the best-established effect, because the interval shows how much uncertainty remains around it.

Relative estimates convey the same broad uncertainty. The risk ratio is 0.848, with a confidence interval from 0.485 to 1.481, and the odds ratio is 0.810, with a confidence interval from 0.398 to 1.649. Each interval includes the value representing no relative difference. The measures use different scales, but neither offers a precise estimate that rules out effects in both directions.

Confidence intervals are affected by the amount of information in the data and by the statistical method. The primary outcome summaries include 90 and 91 participants in the two arms, with 21 and 18 deaths, respectively. The registry record states a target of 360 participants in its study summary and an enrollment of 183, but it does not report the original sample-size justification or explain the difference. It is therefore not possible to determine from the record whether the trial was expected to estimate mortality with a particular precision.

Precision is not the same as importance. A narrow interval can still center on an effect of little practical relevance, while a wide interval may include effects that would matter in either direction. The registry record does not state a threshold for a clinically important mortality difference. The primary result is consequently best conveyed by its estimate and interval together, without interpreting the nonsignificant p-value as evidence of equivalence.

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 participants per arm for these binary outcomes, not total events. They are illustrations based on the observed effect, not a reconstruction of the trial's original design. The assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each outcome, the effect to detect is specified as a fraction of the observed effect.

For any stated effect size, the 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting that effect under the stated assumptions, if the model and assumptions hold. The 90% power column gives the corresponding number per arm for a 90% chance. These are design-planning quantities, not guarantees about the result of a future study. They do not describe the probability that a treatment works or the probability that a particular observed finding is true.

The rows based on 100% of the observed effect use the full effect estimate from the posted comparison as the planning target. Rows based on 75% or 50% of the observed effect use smaller target effects. Smaller effects are harder to distinguish from no difference, so the required number of participants per arm increases as the effect to detect becomes smaller. The numerical values are specific to each endpoint and should be read with the stated assumptions in mind.

The sample-size assumptions for the trial's original design are not reported in the registry record. The brief summary states a target of 360 participants, 180 per arm, but does not report the calculation or its assumptions. The figures in these planning illustrations are not observed power; observed power is not an informative substitute for reading the estimates and confidence intervals from the results.

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 = 0.233; treatment proportion p₁ = 0.198; average p̄ = 0.216.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5815 = 1.1398.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5810 = 0.4890.
4. n = (1.1398 + 0.4890)² / (-0.0355)² = 2,101.4, rounded up to 2,102 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 <- 0.233333333333333                          # control proportion
p1 <- 0.197802197802198                          # 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(2063880)
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 = 2,102 (80% power), 2,813 (90% power)
 75% of observed effect: n per arm = 3,793 (80% power), 5,077 (90% power)
 50% of observed effect: n per arm = 8,657 (80% power), 11,589 (90% power)
power.prop.test: 2101.4 
Simulated power at n = 2,102 per arm: 0.804 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and two secondary outcomes, but it does not report a multiplicity adjustment or a hierarchy for testing the secondary outcomes. Multiplicity matters because testing several outcomes creates more opportunities for a chance result to appear noteworthy. Without a prespecified strategy, unadjusted secondary p-values should not be treated as though they provide the same confirmatory evidence as a single prespecified primary test. The record labels the posted comparison p-values unadjusted and lists no reported secondary analyses.

The original statistical analysis plan is not reported in the registry record. Consequently, the record does not establish which comparisons were prespecified, whether any analysis was intended to be adjusted for baseline characteristics, whether subgroup analyses were planned, or how deviations from the intended treatment timing were to be handled. The summary mentions aims to determine co-factors for mortality, IRIS, and drug toxicity, but no co-factor analyses are posted. Their absence from the posted results should not be filled in by assumption.

Missing-data handling and analysis populations are also not reported in the registry record. The enrollment figure is 183, while the primary outcome denominators are 90 and 91; the registry record does not explain whether these denominators represent all randomized participants, participants with observed outcome status, or another defined analysis population. It does not report the number or reasons for any missing outcomes, imputation methods, or sensitivity analyses. The listed denominator difference should therefore be described without inferring attrition or an intention-to-treat analysis.

The trial is described as randomized and unblinded. The registry record does not report allocation concealment details, adherence summaries, crossover counts, interim analyses, or stopping rules. These are relevant to interpreting how the trial was conducted and analyzed, but their absence from the record does not establish that a particular procedure was or was not used. The posted estimates should be read in the context of these reporting gaps rather than supplemented with assumptions about protocol or analysis.

15. 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: non-mortality sae (24.2%), mortality (23.3%).

The registry record lists serious adverse event summaries by arm, including 34 participants at risk and 10 with other adverse events in the urgent ART arm, and 40 participants at risk and 12 with other adverse events in the early ART arm. It also lists 21 deaths in the urgent arm and 18 in the early arm. The record separately identifies the leading serious-event terms as Non-mortality SAE at 24.2% and Mortality at 23.3%.

These figures should be read as posted event summaries, not as evidence that the treatment timing caused or prevented an event. The record does not explain the definitions behind the serious-event categories, whether participants could contribute to more than one category, or how the listed overall terms relate to the arm-specific summaries. It does not provide enough detail to reconstruct a complete safety profile or compare event severity and timing. The mortality counts also correspond to the primary endpoint; they are not a separate measure of nonfatal harm.

The IRIS and potential drug toxicity outcomes are posted separately as secondary outcomes. Their definitions and event-assessment procedures are not reported in the registry record. Accordingly, the adverse-event figures describe the recorded summaries and should not be interpreted as a definitive causal safety comparison.

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

The posted primary results show 21 deaths among 90 participants assigned to urgent ART and 18 among 91 assigned to early ART. The risk-difference estimate is -0.035 for early ART relative to urgent ART, and its 95% confidence interval ranges from -0.155 to 0.084. The point estimate favors early ART on the risk-difference scale, but the interval includes no difference and effects in either direction. The unadjusted p-value of 0.561 does not provide clear evidence of a difference under the reported comparison.

This result does not establish that the treatment strategies are equivalent. A nonsignificant test is not an equivalence test, and the confidence interval is broad. Nor does the result establish that urgent or early treatment caused the observed difference in deaths. Randomization supports a comparison of assigned groups, but the registry record does not report the analysis population, missing-data handling, adherence, or other details needed to assess the full analysis process.

The secondary results describe IRIS and potential drug toxicity, outcomes that relate to concerns stated in the study rationale. Their estimates are uncertain and their p-values are unadjusted. They should be treated as secondary evidence, particularly because the registry record does not report a multiplicity strategy or a detailed analysis plan. The registry record also does not report outcome definitions or assessment procedures for these endpoints.

More broadly, the posted results address a specific trial population: hospitalized, ART-naïve children with HIV-1 and serious infection, as described in the record. They should not be generalized automatically to other populations, settings, or treatment decisions. The registry record does not provide enough detail to determine how representative the enrolled participants were of other groups.

The most defensible reading is that mortality estimates were imprecise and did not establish a clear difference between the assigned strategies in the posted analysis. The results do not prove absence of an effect, determine which timing strategy is preferable, or settle the possible balance between mortality, IRIS, and drug toxicity. They report what the available registry summaries show, with uncertainty and reporting limitations that remain important to interpretation.

17. Why This Trial Matters Statistically

This trial is statistically notable because its primary comparison is a randomized evaluation of treatment timing in a clinically complex population, while the posted outcome counts are modest relative to the stated target. The registry record lists enrollment of 183, compared with the brief summary's planned 360 participants. The outcome denominators are 90 and 91. These figures help explain why the primary estimate has a broad confidence interval, although the original sample-size justification and the reason for the enrollment difference are not reported.

The comparison also illustrates why the point estimate, confidence interval, and p-value should be read together. The primary point estimate favors early ART on the risk-difference scale, but its interval includes zero and substantial effects in either direction. The p-value alone cannot show whether a difference is important or whether the strategies are equivalent. Precision and effect direction are both necessary to understand what the data can support.

Multiplicity is another important statistical consideration. Alongside mortality, the record lists two secondary outcomes and provides unadjusted comparisons. Those outcomes address concerns about IRIS and potential drug toxicity, but no multiplicity strategy or detailed analysis plan is reported. This makes it especially important to distinguish the primary inference from exploratory secondary patterns.

Finally, the record shows how trial registration summaries can support a useful statistical reading while leaving important interpretive details unresolved. Randomization and the outcome summaries are reported, but analysis populations, missing data, endpoint definitions, and the original planning assumptions are not. A careful interpretation keeps the posted estimates visible while avoiding stronger claims than their precision and reporting detail can support.

18. Limitations

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

The registry record gives limited detail about how the trial was conducted and analyzed. It describes randomization and no masking, but allocation concealment procedures, adherence, crossover, and deviations from the assigned timing are not reported. These details would help clarify how closely the comparison of assigned strategies reflects the treatment each participant actually received.

The primary endpoint timeframe is stated as 6 months post-HAART initiation, while the study summary describes routine follow-up for a maximum of 6 months. The record does not explain the exact outcome ascertainment schedule or how deaths and other events were confirmed. It also does not report how incomplete follow-up was handled. Because the primary denominators total 181 while the enrollment figure is 183, the denominator accounting warrants caution, but the record does not establish why the figures differ.

The brief summary states a planned sample size of 360, with 180 per arm, while recorded enrollment is 183. No original sample-size calculation, precision target, or justification for the target is reported. Without that information, the enrollment difference cannot be explained and the intended statistical operating characteristics of the original design cannot be evaluated from the registry record.

The registry record lists IRIS and potential drug toxicity but does not provide endpoint definitions, grading rules, timing details, or adjudication procedures. It also does not report a multiplicity plan, an analysis population, adjusted estimates, or co-factor analyses. These omissions constrain interpretation of secondary outcomes and prevent assessment of whether the posted analyses followed a prespecified plan. The unblinded design is another relevant limitation, although the record does not describe whether any outcome-assessment safeguards were used.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pediatric Urgent Start of Highly Active Antiretroviral Treatment (HAART) — NCT02063880.
• Registry record last updated 2018-05-14; status last verified 2018-04.
• Results first posted 2017-07-25.
• 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.

22. Record Summary

The registry record describes a completed, randomized, unblinded, parallel-group trial of urgent versus early ART in hospitalized children with HIV-1 and severe co-infections. Urgent HAART was to begin within 48 hours of enrollment; early HAART was to begin 7-14 days after enrollment. The listed enrollment is 183, and the primary outcome is all-cause mortality 6 months post-HAART initiation.

Posted primary outcome counts are 21 of 90 participants in the urgent arm and 18 of 91 in the early arm. The risk difference for early ART relative to urgent ART is -0.035, with a 95% confidence interval from -0.155 to 0.084 and an unadjusted p-value of 0.561. The interval includes no difference and remains compatible with effects in either direction.

The registry record also posts IRIS and potential drug-toxicity outcomes. It does not report the original sample-size justification, detailed analysis plan, missing-data handling, or multiplicity strategy. These omissions, together with the imprecise primary estimate, limit the strength of conclusions that can be drawn from the posted results.