Safety and Efficacy of Switching From Stavudine or Zidovudine to Tenofovir DF in HIV-1 Infected Children: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Switching From Stavudine or Zidovudine to Tenofovir DF in HIV-1 Infected Children (NCT00528957), a randomized phase 3 study. The primary outcome is Percentage of Participants With HIV-1 RNA < 400 Copies/mL at Week 48.

2. Clinical Question

The endpoint focuses on maintaining virologic suppression after a treatment switch. The registry describes the main objective as assessing the efficacy of switching to TDF compared with continuing stavudine or zidovudine in maintaining suppression. The primary outcome uses an intent-to-treat population and counts missing outcomes as failures.

This is a question about the observed endpoint in the groups studied, not a general claim about all children with HIV-1 infection or all treatment settings. The registry record identifies a randomized, open-label study, but does not report detailed eligibility criteria, the rationale for choosing the 48-week assessment, or the non-inferiority margin. Those omissions limit how fully the intended comparison can be reconstructed.

3. Trial Design

The registry describes a Phase III, randomized, open-label, parallel-group study of switching to tenofovir DF versus continuing stavudine or zidovudine in virologically suppressed HIV-infected children taking highly active antiretroviral therapy. The study is listed as completed, with 97 participants enrolled. The recorded study start is 2006-12-28 and primary completion is 2009-04-06.

Randomization means treatment assignment was allocated by chance, rather than chosen solely by participants or clinicians. Open-label means the record identifies no masking; participants and study personnel were not described as blinded. In a parallel design, participants are assigned to a group and the groups are compared over the study. Further operational details of randomization, including sequence generation and allocation concealment, are not reported in the registry record.

The intervention was a switch from stavudine or zidovudine to TDF, while the comparator was continued stavudine or zidovudine. The primary endpoint analysis includes 48 participants in the TDF group and 49 in the continuation group. These endpoint denominators should not be treated as a description of why any enrolled participants were not included in the primary endpoint denominator; reasons are not reported in the registry record.

The registry lists 46 outcome measures and two analyses. The primary outcome assesses HIV-1 RNA below 400 copies/mL at 48 weeks. Other posted outcomes include virologic success at 48 weeks using 400- and 50-copy thresholds, and measures at later follow-up times. Detailed visit schedules, treatment adherence methods, dose information, and the trial's original sample-size justification are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 127 participants were screened.

Randomized Phase (Baseline to Week 48)

Reasons for not completing this period:

First Extension (Week 48 to Week 144)

Reasons for not completing this period:

Second Extension (Week 144 to Week 240)

Reasons for not completing this period:

Third Extension (Week 240 to Week 336)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat, Missing = Failure

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: Randomized and Treated Set: participants who were randomized and received at least 1 dose of study drug

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With HIV-1 RNA < 400 Copies/mL at Week 48, measured over 48 weeks.

The primary endpoint is the percentage of participants with HIV-1 RNA < 400 copies/mL after 48 weeks of exposure to randomized study drug. It is a binary outcome at the participant level: each participant either meets the stated viral-load threshold or does not. The reported percentage expresses how common that outcome was within each group.

Virologic suppression is relevant to the study question because the stated objective was to assess whether switching treatment maintained suppression. The endpoint therefore measures whether the threshold was met at a specified follow-up point, rather than measuring change in viral load as a continuous quantity. The registry defines the primary population as intent-to-treat, with missing outcomes counted as failures. This rule places participants with missing endpoint data in the non-success category for the primary analysis.

Such a threshold-based measure offers a direct way to compare the proportions meeting a prespecified clinical or laboratory criterion. It also discards information about how far an individual measurement lies above or below the threshold. The registry lists the endpoint unit as percentage of participants and gives a 48-week timeframe. The detailed laboratory measurement procedures and the reasons for selecting the 400-copy threshold are not reported in the registry record.

7. Results Posted in the Registry

• Stavudine or Zidovudine: 91.8% (45/49) versus 83.3% (40/48) on control; risk difference 8.5 percentage points (95% CI -4.5 to 21.5), risk ratio 1.10 (0.95–1.28); unadjusted two-proportion z-test p = 0.203.

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.

Virologic Success at 48 Weeks (HIV-1 RNA Cutoff at 400 Copies/mL, Snapshot)

• 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:
  • Stavudine or Zidovudine: 89.6% (43/48) versus 88.6% (39/44) on control; risk difference 0.9 percentage points (95% CI -11.8 to 13.7), risk ratio 1.01 (0.88–1.17); unadjusted two-proportion z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stavudine or Zidovudine and the control. The interval gives the range of effects that remain compatible with the data.

Virologic Success at 48 Weeks (HIV-1 RNA Cutoff at 50 Copies/mL, Snapshot)

• 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:
  • Stavudine or Zidovudine: 81.2% (39/48) versus 75.0% (33/44) on control; risk difference 6.2 percentage points (95% CI -10.7 to 23.2), risk ratio 1.08 (0.87–1.35); unadjusted two-proportion z-test p = 0.468.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stavudine or Zidovudine and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With HIV-1 RNA < 400 Copies/mL at Week 96

• 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:
  • (Stavudine or Zidovudine)/TDF: 85.4% (35/41) versus 81.6% (31/38) on control; risk difference 3.8 percentage points (95% CI -12.6 to 20.2), risk ratio 1.05 (0.86–1.27); unadjusted two-proportion z-test p = 0.650.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between (Stavudine or Zidovudine)/TDF and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend the primary question across different viral-load thresholds and follow-up times. At 48 weeks, the record includes snapshot outcomes using both the 400-copy and 50-copy thresholds; later outcomes include 400-copy assessments at 96 weeks and additional scheduled follow-up times. These outcomes give context about how the recorded suppression pattern was examined beyond the primary endpoint.

Across the secondary results described, the observed percentages in the two groups are broadly similar in scale, and the comparisons remain uncertain. This general pattern is consistent with the primary result in the limited sense that the posted secondary estimates do not resolve a clear group separation. The secondary analyses use endpoint-specific denominators and, for later follow-up, group labels that include participants who continued or switched treatment. They therefore should not be treated as interchangeable with the primary 48-week comparison.

The registry lists 45 secondary outcomes, while not every outcome has detailed comparison results in the posted summary. The full analytic handling of these outcomes, including missing-data conventions and the order in which they were tested, is not reported in the registry record. The 48-week snapshot labels identify a particular assessment approach, but they do not supply all details needed to reconstruct each analysis.

In general, testing many secondary outcomes raises multiplicity concerns: the more comparisons considered, the greater the chance that some results may appear notable by chance. Unless a multiplicity strategy is specified, secondary findings are usually more exploratory than the primary result. The registry record does not report an adjustment strategy. The secondary outcomes can help describe the breadth of follow-up, but they should not be treated as independent confirmation of the primary finding or as a replacement for its prespecified interpretation.

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

• Virologic Success at 48 Weeks (HIV-1 RNA Cutoff at 400 Copies/mL, Snapshot)
• Virologic Success at 48 Weeks (HIV-1 RNA Cutoff at 50 Copies/mL, Snapshot)
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at Week 96
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at Week 144
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at 192 Weeks
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at 240 Weeks
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at 288 Weeks
• Percentage of Participants With HIV-1 RNA < 400 Copies/mL at 336 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome summarized as a percentage: the proportion in each group who had HIV-1 RNA < 400 copies/mL at 48 weeks. A group percentage is an estimate from the participants included in that group’s analysis. The primary analysis population is described as intent-to-treat, with missing outcomes treated as failures. In general, this approach keeps the analysis linked to randomized assignment and defines how missing endpoint observations affect the success count.

A risk difference compares two group proportions by subtraction. Its sign depends on which group is placed first. The re-calculated risk difference is 0.085 when expressed as continuation minus TDF; the sponsor reports -8.5 percentage points in the opposite direction. The magnitude and interval can therefore be read consistently only after noting the contrast order. A risk difference is directly expressed on the percentage-point scale, unlike a ratio measure, and can be interpreted as a difference in the observed proportions.

The registry's sponsor-reported primary analysis is described as a normal approximation and reports a difference in percentages between groups with a 95% confidence interval. In general, a normal-approximation method uses an approximate sampling distribution to estimate uncertainty around a contrast. The recalculated analysis uses posted summary counts and is unadjusted. It does not replace the sponsor's analysis, which takes precedence when comparing against the trial's own reported result.

In general, a confidence interval gives a range of values compatible with the data and the method's assumptions at the stated confidence level. It is not a range containing a specified proportion of individual outcomes, and it does not assign a probability to the true effect after the data have been observed. For a difference, an interval spanning zero includes no difference as one possibility. That observation alone does not determine whether a non-inferiority or equivalence criterion has been satisfied.

Non-inferiority analyses ask whether an intervention's outcome is not worse than a comparator by more than a prespecified margin. Equivalence analyses generally seek to rule out differences beyond prespecified bounds in either direction. Both rely on a clearly specified margin and a planned analysis approach. Although the reported primary analysis is labeled non-inferiority or equivalence, the margin, the decision rule, and the detailed statistical plan are not reported in the registry record. A reader cannot infer those elements from the label alone.

The registry gives a p-value of 0.203 for the unadjusted re-calculation, while the sponsor-reported primary analysis has no p-value listed. In general, a p-value measures how unusual the data would be under a specified null hypothesis and model. It does not describe effect size, precision, or the probability that a hypothesis is true. The confidence interval and endpoint percentages provide complementary information about the estimate and its uncertainty.

What does a binary endpoint leave out?

Reducing a laboratory measure to whether it is above or below a cutoff makes the endpoint easy to interpret as a proportion meeting the criterion. It also treats values close to the threshold differently from values far from it, while not showing the degree of difference between those values. The registry record reports the threshold and endpoint definition, but does not report further analyses of the underlying continuous viral-load measurements.

What does missing equals failure mean?

For the primary endpoint, missing outcomes are classified as failures. This is an explicit analysis rule and can affect the percentage if endpoint status is unavailable. It does not reveal how many observations were missing or why; those details are not reported in the registry record. The separately listed snapshot outcomes do not establish that the primary missing-data rule was also used for every secondary analysis.

Why does over-dispersion matter?

Over-dispersion is a general issue for count or rate models when variation exceeds what a chosen model expects. The primary endpoint is reported as a percentage of participants, not as a count rate with a dispersion estimate, and the registry does not report an over-dispersion model for it. It is therefore not a stated feature of this primary analysis. More broadly, using a model that does not account for extra variability can make uncertainty appear too small; model choice should match the outcome and design.

Finally, statistical interpretation depends on design and reporting, not on a single calculation. Random assignment supports a group comparison, while the open-label designation and unreported methodological details leave questions about conduct and analysis unresolved. The numerical results describe the posted endpoint and should not be extended beyond those data.

11. Confidence Intervals and Precision

The primary group estimates have 95% confidence intervals: 69.8% to 92.5% for TDF and 80.4% to 97.7% for continued stavudine or zidovudine. The intervals communicate uncertainty around each estimated percentage. Their width reflects that the percentages are estimates from groups of 48 and 49 participants, rather than exact values for a larger population.

For the contrast, the unadjusted re-calculated risk difference is 0.085, with a 95% confidence interval from -0.045 to 0.215. The sponsor's reported contrast is -8.5 percentage points, with a 95% confidence interval from -21.5 to 4.5. The contrast directions are reversed, and the sponsor's own analysis takes precedence. Both intervals include no difference under their respective contrast conventions, while also allowing differences in either direction.

In general, precision is about how narrowly a result is estimated, not whether the result is important. A confidence interval that spans a broad range leaves more uncertainty about the effect's size. An interval crossing no difference does not prove equality; it indicates that the data and method do not rule out no difference at the stated confidence level. Conversely, an interval should not be interpreted as a guarantee that the true value lies within its endpoints.

The sponsor analysis is explicitly reported with a 95% confidence interval. The registry record does not report the non-inferiority margin needed to judge the interval against a trial-specific criterion. Precision can therefore be described from the interval, but a formal non-inferiority conclusion cannot be reconstructed from the interval alone.

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 assumptions. The original sample-size justification and design assumptions are not reported in the registry record. For the primary contrast, the planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; it considers detecting the stated fraction of the observed effect.

The 80% power column gives the estimated number of participants per arm under those assumptions for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not descriptions of what happened in the trial. They are not observed power.

For the primary endpoint, planning for 100% of the observed effect gives 235 participants per arm for 80% power and 314 participants per arm for 90% power. Planning for 75% of the observed effect gives 449 participants per arm for 80% power and 601 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,078 participants per arm for 80% power and 1,443 participants per arm for 90% power. Smaller effects require more participants to detect under the same planning assumptions.

These figures are hypothetical planning scenarios based on the observed group difference, not a retrospective judgment about the study's success. They do not show that the trial had a particular probability of detecting an effect, and they should not be read as evidence for or against the study's findings. The planning display uses participants per arm for this outcome, not total events.

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 = 0.833; treatment proportion p₁ = 0.918; average p̄ = 0.876.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4663 = 0.9140.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4624 = 0.3892.
4. n = (0.9140 + 0.3892)² / (0.0850)² = 234.9, rounded up to 235 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 <- 0.833333333333333                          # control proportion
p1 <- 0.918367346938776                          # 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(528957)
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 = 235 (80% power), 314 (90% power)
 75% of observed effect: n per arm = 449 (80% power), 601 (90% power)
 50% of observed effect: n per arm = 1,078 (80% power), 1,443 (90% power)
power.prop.test: 234.9 
Simulated power at n = 235 per arm: 0.811 (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 sponsor-reported primary analysis gives a difference in percentages of -8.5, with a 95% confidence interval from -21.5 to 4.5. It is labeled as a non-inferiority or equivalence analysis and uses a normal approximation. The recalculated unadjusted contrast is a risk difference of 0.085, with a 95% confidence interval from -0.045 to 0.215 and p = 0.203.

The apparent sign reversal reflects the contrast order: the recalculation expresses continued stavudine or zidovudine relative to TDF, while the sponsor result expresses the groups in the opposite direction. The posted sponsor result is the trial's own analysis and takes precedence over the simple unadjusted recalculation. The latter is useful as a check based on the reported summary counts, but it may not reproduce all details of the sponsor's analytic procedure.

The registry record does not report the non-inferiority margin, detailed model specification beyond the normal approximation, or the full analysis plan. Consequently, the sponsor's label and confidence interval can be described, but the formal decision rule cannot be independently evaluated from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is identified as intent-to-treat, with missing outcomes counted as failures. This is important because it specifies how unavailable primary endpoint status contributes to the analysis. The registry record does not report how many primary outcomes were missing, why they were missing, or whether additional sensitivity analyses examined alternative assumptions.

Missing-data handling for the secondary outcomes is not reported in the registry record. Some secondary outcomes are explicitly labeled as snapshot measures, but the label alone does not describe every rule for handling missing data, treatment changes, or assessments outside the stated window. The secondary endpoint denominators differ from the primary denominators; the registry record does not state the reasons for those differences.

The registry lists many secondary outcomes, including repeated assessments over time and more than one viral-load threshold. In general, testing multiple endpoints can increase the risk of chance findings if no adjustment or hierarchy is used. The multiplicity strategy, any hierarchy among outcomes, and whether secondary analyses were considered confirmatory are not reported in the registry record. Secondary p-values and confidence intervals should therefore be interpreted with caution, even when an individual result appears noteworthy.

The primary analysis is labeled non-inferiority or equivalence, but the margin and the planned decision procedure are not reported in the registry record. The record also does not provide a full statistical analysis plan, details of interim analyses, or the original sample-size justification. These omissions make it difficult to assess whether all analyses followed prespecified rules or how the primary claim was intended to be judged.

In general, these reporting gaps do not invalidate the posted numbers, but they narrow the conclusions that can be drawn from them. A reader can describe the endpoint estimates and intervals, while recognizing that missing-data sensitivity, multiplicity control, and trial-specific decision criteria cannot be independently assessed from the registry record.

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: pneumonia (2.2%), abortion spontaneous (2.2%), pharyngotonsillitis (2.1%), lymphadenitis (2.0%), asthmatic crisis (2.0%).

The registry reports serious adverse events affecting 2 of 48 participants in the TDF group and 2 of 49 participants in the stavudine or zidovudine group. It also lists an All TDF group with 15 of 89 participants affected. The record reports zero deaths in each of these groups. These are reported group counts, not estimates of a causal treatment effect.

For other adverse events, the registry reports 37 of 48 participants in the TDF group and 35 of 49 participants in the continuation group, with 82 of 89 in the All TDF group. The record lists serious-event terms and percentages including pneumonia at 2.2%, abortion spontaneous at 2.2%, pharyngotonsillitis at 2.1%, lymphadenitis at 2.0%, asthmatic crisis at 2.0%, and abdominal adhesions at 1.1%.

These figures require care: the record does not provide enough detail to attribute individual events to treatment, establish their timing, or compare event risk with an adjusted analysis. The All TDF group is a separately listed group and should not be treated as an additional randomized comparison. The safety counts describe what was posted, not whether a treatment caused an event or how clinically important any individual event was.

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

The results describe the proportion meeting a viral-load threshold at 48 weeks among children in the two randomized groups. The TDF group estimate was 83.3%, and the continued stavudine or zidovudine group estimate was 91.8%. The confidence intervals and the contrast interval show that the estimates are uncertain, with plausible values on either side of no difference.

The registry labels the primary analysis as non-inferiority or equivalence, but does not report the margin or the full decision rule. The observed percentages and confidence interval therefore cannot alone establish a formal conclusion under those frameworks. The recalculated p-value is unadjusted and is not a test of whether the treatments are equivalent. The sponsor's own reported analysis takes precedence over the unadjusted re-calculation.

The findings do not establish a general conclusion for populations or settings beyond the trial described. The registry record identifies virologically suppressed children taking highly active antiretroviral therapy, but detailed eligibility criteria and several aspects of conduct are not reported. The endpoint is a threshold-based measure at a specified follow-up time; it does not show the full pattern of viral-load measurements or every aspect of health and treatment experience.

The study is randomized and open-label. Randomization is a design feature intended to make group comparisons informative, while lack of masking can matter for aspects of study conduct or outcome assessment. The registry does not provide enough detail to assess those issues in depth. The reported safety counts likewise do not by themselves demonstrate cause and effect.

In short, the posted results support a precise description of the measured endpoint and its uncertainty, but not a claim that the treatments are identical, that one is better, or that the result applies universally. Further interpretation depends on the unreported non-inferiority margin, analysis plan, missing-data details, and multiplicity approach.

18. Why This Trial Matters Statistically

This trial raises an important statistical distinction between observing similar-looking percentages and demonstrating equivalence or non-inferiority. The primary estimates are 83.3% and 91.8%, but a formal conclusion under either framework depends on a prespecified margin and analysis plan. Those details are not reported in the registry record. Without them, the outcome can be described, but the intended decision threshold cannot be reconstructed.

The confidence interval for the group contrast emphasizes the role of precision. It spans no difference and also allows a range of contrasts in either direction. That uncertainty matters especially when a study is designed to evaluate whether a switch preserves an outcome within an acceptable boundary. A point estimate by itself is not enough to establish that boundary has been met.

The primary analysis also illustrates how an explicit missing-data rule affects interpretation. Missing outcomes are counted as failures in the intent-to-treat analysis, but the number and reasons for missing observations are not reported. Clear reporting of those details would help readers assess how the endpoint definition and available data relate.

Finally, the registry includes multiple secondary outcomes across thresholds and follow-up times. Their breadth can add context, but without a reported multiplicity strategy they should not carry the same interpretive weight as a well-defined primary analysis. Taken together, these features make the study a useful example of why effect estimates, confidence intervals, design labels, missing-data rules, and reporting completeness need to be considered together.

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 does not report the non-inferiority margin or the detailed decision rule for the primary analysis, despite labeling the analysis non-inferiority or equivalence. This prevents independent assessment of whether the primary interval met the study's intended criterion. The full statistical analysis plan and the original sample-size justification are also not reported.

The primary endpoint uses intent-to-treat with missing outcomes treated as failures, but the number and reasons for missing outcomes are not reported. The missing-data rules for secondary outcomes are also not reported. This makes it difficult to assess how endpoint availability may have affected the primary and secondary percentages or whether alternative assumptions were examined.

The trial was open-label, and the registry record does not report details of allocation concealment, outcome assessment procedures, adherence measurement, or other methods that could help readers evaluate conduct. The randomized comparison is clear at a broad level, but those operational details are unavailable in the registry record.

The secondary outcome set includes multiple thresholds and follow-up times, but a multiplicity strategy is not reported. The record does not provide enough information to distinguish confirmatory secondary analyses from exploratory ones. Several posted outcomes also use different denominators or group labels; the reasons and analysis rules behind those differences are not reported.

These limitations do not alter the numerical results as posted, but they restrict the strength and scope of interpretation. They are especially relevant to formal non-inferiority claims, missing-data sensitivity, and claims based on secondary results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Switching From Stavudine or Zidovudine to Tenofovir DF in HIV-1 Infected Children — NCT00528957.
• Registry record last updated 2018-03-14; status last verified 2018-02.
• Results first posted 2012-03-22.
• 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

NCT00528957 is a completed Phase III randomized, open-label, parallel-group study sponsored by Gilead Sciences. It enrolled 97 participants and compared switching from stavudine or zidovudine to tenofovir DF with continuing stavudine or zidovudine in virologically suppressed HIV-infected children taking highly active antiretroviral therapy.

The primary outcome was the percentage with HIV-1 RNA < 400 copies/mL at 48 weeks, analyzed in an intent-to-treat population with missing outcomes counted as failures. The posted group estimates were 83.3% for TDF and 91.8% for continued stavudine or zidovudine. The sponsor reported a -8.5 percentage-point contrast with a 95% confidence interval from -21.5 to 4.5; the unadjusted re-calculation takes the opposite contrast direction and does not replace the sponsor analysis.

The record lists multiple secondary outcomes and safety counts. Important details, including the non-inferiority margin, original sample-size justification, multiplicity strategy, and several missing-data procedures, are not reported in the registry record.