A Study to Evaluate the Safety and Efficacy of Adding Enfuvirtide to Oral Highly Active Antiretroviral Therapy (HAART) in Human Immunodeficiency Virus (HIV) Patients With Prior Treatment Experience: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Safety and Efficacy of Adding Enfuvirtide to Oral Highly Active Antiretroviral Therapy (HAART) in Human Immunodeficiency Virus (HIV) Patients With Prior Treatment Experience (NCT00487188), a randomized phase 4 study. The primary outcome is Number of Participants With Viral Suppression: HIV-1 RNA < 50 Copies/mL During the Induction Phase.

2. Clinical Question

The question concerns a specific measure of viral suppression at a specified point in the induction phase. A participant counted as a responder needed to meet the suppression threshold by Week 24 and have that response confirmed at Week 28. The registry description specifies that the two consecutive assessments had to be at least 28 days apart. Participants who discontinued or did not respond to assigned treatment by Week 28 were counted as non-responders.

This is an assignment-based comparison of the two treatment strategies, not a comparison restricted to participants who completed treatment or maintained suppression through the full treatment period. The registry record also lists outcomes for viral load at a less stringent threshold, changes in viral load and CD4+ cell counts, and measures at Week 48. Those outcomes provide related but distinct information; they do not replace the primary induction-phase question.

3. Trial Design

The registry record describes a phase 4, randomized, controlled, parallel-group study with no masking. Its official title characterizes the study as an intensification strategy: enfuvirtide was added to oral HAART and compared with oral HAART alone in treatment-experienced patients. The record lists HIV infections as the condition and Hoffmann-La Roche as the sponsor. The status is completed.

Participants were assigned to ENF plus HAART or HAART alone. The intervention description states that ENF was given by subcutaneous injection at 90 mg twice a day, alongside an oral HAART regimen, for up to 48 weeks. The HAART-only regimen consisted of 3-5 antivirals and was also planned for up to 48 weeks. The registry record reports enrollment of 47, with 31.0 assigned to ENF plus HAART and 16.0 to HAART.

The open-label design means masking was not used, according to the registry record. The record does not report further details about the allocation sequence, concealment of allocation, or procedures intended to reduce bias in outcome assessment. Those details should not be inferred from the description of randomization alone.

The primary endpoint concerns the induction phase, with response assessed by Week 24 and confirmed at Week 28. This timing is distinct from the treatment period of up to 48 weeks and from the registry’s listed Week 48 outcomes. The record also separates induction and maintenance-phase outcomes. It does not report a full account of how participants entered or moved between those phases, so phase-specific results should be read in light of their stated populations and denominators rather than assumed to represent the same group at every assessment.

The registry record does not report the trial’s original sample-size justification, planned statistical analysis details, or whether interim analyses were planned. The planning illustrations associated with the posted results are not a substitute for those protocol details.

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: In the Induction Phase participants were randomized (2:1 ratio) to receive ENF + HAART or HAART. In the Maintenance Phase participants in the HAART group who responded (viral load \< 50 copies/mL) continued to receive HAART; those who responded in the ENF + HAART group were re-randomized (1:1 ratio) to receive ENF + HAART or HAART (ENF removed).

Induction Phase

Reasons for not completing this period:

Maintenance Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Population 1 (ITT1) population (patients evaluable for efficacy in the induction phase)

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 Number of Participants With Viral Suppression: HIV-1 RNA < 50 Copies/mL During the Induction Phase, measured over From Baseline 1 to Week 28.

The primary endpoint counts participants who achieved HIV-1 RNA < 50 copies/mL during the induction phase. The registry defines a responder as someone who reached the threshold by Week 24 at the latest and had the response confirmed at Week 28, using two consecutive assessments at least 28 days apart. Participants who discontinued or had not responded to assigned treatment by Week 28 were classified as non-responders. The timeframe is listed as Baseline 1 to Week 28, and the population is the ITT1 population described as patients evaluable for efficacy in the induction phase.

This endpoint turns a laboratory measure of viral load into a response count for each assigned group. A suppression threshold gives a clear criterion for classifying response, while confirmation at a later assessment is intended to distinguish a sustained finding from a single assessment. Counting discontinuations and non-response as failures also makes the endpoint reflect more than the measured viral load among people who remained on treatment and had an observed response.

As a general statistical point, binary response outcomes are straightforward to interpret as counts or proportions, but they discard detail about how far individual viral loads changed and when suppression occurred within the allowed period. The registry lists time-to-suppression and continuous viral-load change as separate outcomes, which address different aspects of response. The primary count alone does not describe the magnitude of viral-load change, durability through Week 48, or other clinical outcomes.

7. Results Posted in the Registry

• HAART: 50.0% (8/16) versus 64.5% (20/31) on control; risk difference -14.5 percentage points (95% CI -44.2 to 15.2), risk ratio 0.78 (0.44–1.35); unadjusted two-proportion z-test p = 0.337.

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 Viral Suppression HIV-1 RNA < 400 Copies/mL During the Induction Phase

• 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:
  • HAART: 50.0% (8/16) versus 67.7% (21/31) on control; risk difference -17.7 percentage points (95% CI -47.3 to 11.8), risk ratio 0.74 (0.43–1.28); unadjusted two-proportion z-test p = 0.236.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HAART and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Week 24 in Viral Load

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • HAART: mean -1.16 versus -1.40 on control; difference 0.25 (95% CI -0.47 to 0.96), standardized effect d = 0.20; z-test p = 0.501.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HAART and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Induction Phase Participants With Viral Load < 50 Copies/mL at 48 Weeks

• 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:
  • HAART: 25.0% (4/16) versus 45.2% (14/31) on control; risk difference -20.2 percentage points (95% CI -47.7 to 7.4), risk ratio 0.55 (0.22–1.41); unadjusted two-proportion z-test p = 0.178.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HAART and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes generally point in the same numerical direction as the primary comparison for viral suppression: the ENF plus HAART group had more participants meeting the less stringent suppression threshold during induction and a higher reported percentage meeting the stricter threshold at Week 48. The continuous viral-load change estimates also numerically favor a larger reduction with ENF plus HAART. These outcomes are related to the primary question but use different definitions, time points, and measurement scales.

This broad directional pattern is not the same as a definitive confirmation of the primary result. The secondary comparisons are also imprecise, and their unadjusted p-values do not establish clear differences. The registry record does not list reported analyses for the secondary outcomes, and the available outcomes do not show a consistent, comprehensive statistical analysis across every listed measure. Their role is best viewed as supplementary context rather than independent proof.

General statistical principle: when many outcomes are examined, the chance of encountering at least one apparently unusual result can increase, even if none of the underlying effects is real. Adjusting for multiple comparisons can address that issue, but the registry record does not report a multiplicity adjustment or a prespecified hierarchy among the secondary endpoints. Accordingly, unadjusted secondary findings carry less weight than a single prespecified primary comparison and should not be treated as conclusive on their own.

These measures also answer different scientific questions. A threshold response does not convey the size of viral-load change, and a Week 48 outcome is not interchangeable with an induction-phase response. CD4+ cell-count and time-to-event measures add other dimensions. A reader should consider each in its stated timeframe and population rather than combining them into one overall claim.

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

• Time to Achieving HIV-1 RNA < 50 Copies/mL During the Induction Phase
• Number of Participants With Viral Suppression HIV-1 RNA < 400 Copies/mL During the Induction Phase
• Change From Baseline to Week 24 in Viral Load
• Change From Baseline to Week 24 in Cluster Differentiation Antigen Four Positive (CD4+) Cell Counts
• Percentage of Induction Phase Participants With Viral Load < 50 Copies/mL at 48 Weeks
• Percentage of Maintenance Phase Participants With Viral Load < 50 Copies/mL at 48 Weeks
• Change From Baseline to Week 48 in Cluster Differentiation Antigen Four Positive (CD4) Cell Counts
• Time to Loss of Viral Response During the Maintenance Phase

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion meeting a binary outcome in one group with the proportion in another. In the primary comparison, the reported direction is HAART minus ENF plus HAART. A negative estimate therefore corresponds to a lower observed response proportion in the HAART group. This direction is a matter of the comparison’s ordering; reversing the order would reverse the sign without changing the underlying group results.

Risk differences stay on the scale of proportions. They describe an absolute contrast between groups, rather than a relative ratio. This can make them directly useful for understanding how far apart the observed response proportions are. The value remains an estimate from the trial, not a guarantee of the difference that would occur in another study or population.

What does the confidence interval add?

A confidence interval describes uncertainty around an estimated effect under the statistical method used. It gives a range of effect values compatible with the data and that method, rather than a range containing a known fixed proportion of individual outcomes. A wide interval indicates limited precision. When an interval for a difference spans no difference, the data are compatible with both some advantage for either group and little or no difference.

The primary interval extends from -0.443 to 0.152 around the estimate of -0.145. Its width is important: the point estimate alone would hide how uncertain the comparison is. The interval does not show that all values within it are equally plausible, nor does it identify which effect is true. It helps readers judge what the study can and cannot distinguish.

How should the p-value be read?

The primary unadjusted p-value is 0.337. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model, given the test’s assumptions. It is not the probability that the null hypothesis is true, the probability that the result is due to chance, or a measure of the size or clinical importance of an effect.

The registry record does not report a full analysis plan or a multiplicity procedure. The reported p-value should therefore be read as an unadjusted result, not as evidence that all uncertainty or all possible comparisons have been accounted for. The p-value and confidence interval provide related but different information: the interval emphasizes the range of effect sizes compatible with the data, while the p-value summarizes evidence against a null value under a test.

Why does the endpoint definition affect the analysis?

The endpoint is binary: each participant is classified as a responder or non-responder according to the registry definition. Requiring a response by Week 24 and confirmation at Week 28 makes the endpoint dependent on assessments at more than one time. Counting those who discontinued or did not respond by Week 28 as non-responders incorporates those cases into the response classification rather than simply omitting them.

That rule does not by itself answer every question about missing data. The registry record does not report details about the number or timing of missing measurements, other missing-data rules, or sensitivity analyses. The ITT1 population is described as patients evaluable for efficacy in the induction phase, so readers should not assume from the label alone that every enrolled participant contributed to every analysis.

What is the role of randomization and masking?

Random assignment is intended to make treatment groups comparable in expectation, including with respect to characteristics that are measured and those that are not. In a small study, randomization does not ensure that the realized groups are balanced on every characteristic. The registry record identifies the trial as randomized but does not report the sequence-generation or allocation-concealment methods.

Masking was listed as none. Lack of masking may affect behavior, treatment decisions, reporting, or follow-up, depending on the outcome and study procedures. The primary endpoint uses a laboratory threshold, which is less directly subjective than a symptom rating, but no further information about blinded laboratory assessment is reported in the registry record. These design features inform confidence in the result; they do not change the observed counts.

What do the secondary analyses contribute?

Secondary endpoints cover related but distinct questions, including a less stringent viral suppression threshold, viral-load and CD4+ cell-count changes, response at Week 48, and time-to-event outcomes. Continuous outcomes such as change in viral load summarize magnitude of change, while binary outcomes classify participants according to a threshold. Time-to-event outcomes incorporate when an event occurs, subject to their event definitions and analysis methods.

The registry lists 14 outcome measures and reports 13 secondary outcomes as posted. The record does not list reported analyses for the secondary outcomes. The statistics available for selected secondary measures therefore should not be mistaken for a complete analysis plan or a complete account of all planned comparisons. Because multiple outcomes can generate multiple opportunities for apparently notable findings, unadjusted secondary results need cautious interpretation.

General statistical principle: when a count outcome is analyzed, the amount of information depends on the number of events and the group sizes; for continuous measures, it also depends on variability. The posted endpoint summaries support the stated comparisons, but they do not reveal every modeling choice, adjustment, or assumption used in the trial’s original analysis. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.145, and its 95% confidence interval runs from -0.443 to 0.152. The interval includes no difference and extends in both directions around that point. This means the observed estimate is not precise enough to rule out a range of materially different group contrasts. It is not appropriate to read the point estimate alone as the settled effect.

The amount of information behind the comparison is limited by the reported arm sizes and response counts: 31.0 participants and 20.0 responders in the ENF plus HAART group, and 16.0 participants and 8.0 responders in the HAART group. A small set of observations can yield an estimate that changes noticeably with the outcomes of a few participants. The confidence interval reflects this uncertainty in the primary comparison.

A confidence interval is not a prediction interval for future participants, and it does not say that there is a 95% probability the true effect lies inside this particular interval. In general, it describes the uncertainty produced by a method applied to data under its assumptions. The registry record does not report enough information to assess all assumptions or any adjustments used in the original statistical analysis.

Other reported endpoints also have uncertainty, and their scales differ. A confidence interval for a mean difference in viral-load change cannot be interpreted in the same way as a risk difference for a binary suppression outcome. Precision should be judged for each outcome using its own estimate, scale, and interval. The small trial size and limited event counts constrain how narrowly these data can estimate treatment contrasts.

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 80% power and participants per arm for 90% power. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The registry record does not report the original design assumptions or sample-size justification for the trial.

The 80% power column represents an illustrative group size intended to give an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the method’s assumptions held. The 90% column expresses the same idea with a higher target chance of detection, which generally requires more participants. These are planning calculations, not the trial’s observed power.

Rows that plan for 75% or 50% of the observed effect use smaller effects than the full observed effect. Smaller effects are harder to distinguish from random variation, so the corresponding planning figures require more participants per arm. The figures are illustrations based on the observed estimate, not evidence that an effect of that size is established or likely to recur.

For binary outcomes and continuous outcomes, the figures refer to participants per arm. The general planning description specifies that time-to-event calculations instead give total events, but the displayed planning examples concern the listed binary or continuous comparisons. Reading these numbers as total participants would misstate the planning unit. The trial’s enrollment and actual assigned group sizes are separate from these hypothetical planning scenarios.

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 = 0.645; treatment proportion p₁ = 0.500; average p̄ = 0.573.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6996 = 1.3712.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6920 = 0.5824.
4. n = (1.3712 + 0.5824)² / (-0.1452)² = 181.1, rounded up to 182 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 <- 0.645161290322581                          # control proportion
p1 <- 0.5                          # 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(487188)
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 = 182 (80% power), 242 (90% power)
 75% of observed effect: n per arm = 320 (80% power), 427 (90% power)
 50% of observed effect: n per arm = 709 (80% power), 948 (90% power)
power.prop.test: 181.1 
Simulated power at n = 182 per arm: 0.805 (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 identifies a primary endpoint and lists multiple secondary outcomes, but it does not report a multiplicity-control strategy, a testing hierarchy, or an adjustment for examining multiple endpoints. It also does not report a complete statistical analysis plan. Without those details, the interpretation of individual secondary p-values is limited: an unadjusted result does not account for the possibility that many comparisons were examined.

The record does not report whether interim analyses were planned or performed, whether stopping boundaries were used, or whether any analyses were changed after trial commencement. These protocol and analysis details should not be inferred. The posted status is completed, but that status does not establish what monitoring or interim procedures occurred.

Missing-data information is also limited. The primary endpoint description states that participants who discontinued or did not respond by Week 28 were classified as non-responders. It does not report the amount or pattern of missing viral-load assessments, the specific handling of other missing measurements, or sensitivity analyses evaluating alternative assumptions. The primary analysis population is described as ITT1 patients evaluable for induction-phase efficacy, which does not by itself clarify whether all enrolled or randomized participants were included.

The registry record lists phase-specific safety denominators and maintenance groups, but does not fully explain how participants entered each maintenance group or how missing follow-up affected those summaries. The analysis populations for every secondary endpoint are not specified in the posted results. These omissions matter because populations and missing-data rules can affect both the estimated effect and its precision.

These gaps do not invalidate the posted counts, but they limit independent assessment of how comprehensively the analyses followed the original plan and how robust the results are to alternative assumptions. The registry record does not report these details, so conclusions should remain tied to the endpoints and summaries that are actually posted.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infection (11.1%), anal cancer (11.1%), calculus ureteric (11.1%), pneumonia (10.0%), hepatic function abnormal (10.0%).

The registry lists serious adverse event counts separately for induction and maintenance groups. During induction, serious adverse events affected 3 of 29 participants in the ENF plus HAART group and 3 of 18 in the HAART group. In maintenance, the listed counts are 2 of 10 for ENF plus HAART, 3 of 9 for HAART after ENF was removed, and 0 of 8 for HAART. These are phase-specific summaries, with denominators that differ across groups and phases.

Those counts should not be treated as a simple randomized comparison across all groups. The maintenance groups include different treatment descriptions, and the registry record does not fully explain the transitions into those groups. The listed denominators also differ from the primary efficacy group sizes. A direct comparison requires attention to the analysis population, time at risk, and the way adverse events were collected; those details are not fully reported in the registry record.

The record lists serious adverse-event terms including infection, anal cancer, calculus ureteric, pneumonia, hepatic function abnormal, and respiratory distress, with percentages attached to the terms. It does not provide enough context in the posted term list to assign each percentage to a treatment group or interpret it as a comparative rate. Death counts are not reported in the registry record. These safety summaries describe recorded events and do not establish that a treatment caused an event or that the groups had equivalent safety.

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

The primary result is a comparison of confirmed viral suppression during the induction phase among the stated efficacy population. Numerically, more participants in the ENF plus HAART group met the responder definition than in the HAART group. The estimated risk difference favors the combination group, but the confidence interval includes no difference and extends to effects in either direction. The result is therefore uncertain and should not be described as proof of a difference or proof of equivalence.

The finding applies to the endpoint definition, treatment assignments, and study population described in the registry record. It does not answer whether either treatment strategy produces a durable response for every participant, whether effects persist through all later follow-up, or whether there are differences in outcomes not reported in the registry. Week 48 and maintenance measures are separate outcomes and require their own cautious interpretation.

The trial’s randomized design is relevant to comparing assigned strategies, while its open-label status, small group sizes, and incomplete reporting of analysis details constrain interpretation. The primary endpoint is based on a laboratory threshold, but the record does not report all procedures for assessment or missing data. Statistical uncertainty and reporting gaps remain even when an endpoint is clearly defined.

In general, statistical evidence and clinical importance are not identical. A point estimate can be clinically relevant yet imprecise, and an apparently favorable numerical direction does not establish that the effect is reliable or meaningful in practice. The posted data do not support medical advice or a treatment recommendation. They describe one trial’s observed response counts and the uncertainty around its comparison.

The result also should not be generalized automatically to other populations, treatment histories, regimens, or settings. The record describes treatment-experienced patients and the particular strategies studied; it does not provide evidence for groups or treatment approaches outside that scope.

17. Why This Trial Matters Statistically

This trial illustrates why the effect estimate, its uncertainty, and the endpoint definition need to be read together. The primary response count is easy to understand, but the contrast is imprecise. A directionally favorable point estimate does not by itself show that the underlying difference is reliable, especially when the interval allows a broad range of effects.

It also shows how analysis populations and endpoint rules shape interpretation. Discontinuations and non-response by Week 28 were classified as failures, while the stated population was ITT1 patients evaluable for induction-phase efficacy. These details affect what the response proportion represents. Clear reporting of who contributed to each analysis, and how missing measurements were handled, is essential for understanding a trial result.

Multiple endpoints can enrich interpretation by examining response thresholds, continuous changes, later outcomes, and safety. They can also create multiplicity concerns. Without a reported testing hierarchy or adjustment, secondary findings are best treated as supporting context rather than as multiple independent confirmations.

Finally, the planning illustrations emphasize that study size depends on the effect a future study aims to detect. Smaller target effects require more participants per arm under the stated assumptions. The original trial’s design assumptions are not reported, so the illustrations should not be mistaken for its planned sample size rationale. Together, these points make the record useful for learning how design, analysis, precision, and reporting completeness jointly shape statistical interpretation.

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 enrollment is limited, and the assigned groups are unequal in size. This restricts the information available for estimating a treatment contrast and contributes to the wide uncertainty around the primary result. The response counts are also limited, so the estimate may be sensitive to outcomes among a small number of participants.

The trial was open-label. The primary outcome is based on viral-load measurements rather than a subjective rating, but open-label conduct may still affect study behavior, care decisions, follow-up, or other aspects of outcome collection. The registry record does not report whether laboratory assessment was blinded or what safeguards were used.

Important design and analysis details are not reported in the registry record, including allocation procedures, the original sample-size justification, a complete statistical analysis plan, interim-analysis procedures, and a multiplicity strategy. The record also provides limited detail about missing data and the exact analysis populations for secondary measures. These omissions make it harder to evaluate whether the posted analyses reflect a prespecified plan and how sensitive they are to alternative assumptions.

The induction and maintenance results use different phase-specific populations and denominators. The registry record does not fully explain how participants entered the maintenance groups, including the group described as HAART after ENF was removed. This limits direct interpretation of phase-to-phase comparisons. The safety summaries are similarly descriptive and do not establish comparative risk or causation.

Finally, the posted outcomes cover only the measures and timeframes listed in the registry record. They do not provide a complete picture of all possible benefits, harms, durability, or outcomes beyond the study’s reported follow-up.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Evaluate the Safety and Efficacy of Adding Enfuvirtide to Oral Highly Active Antiretroviral Therapy (HAART) in Human Immunodeficiency Virus (HIV) Patients With Prior Treatment Experience — NCT00487188.
• Registry record last updated 2015-08-13; status last verified 2015-07.
• Results first posted 2011-09-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed phase 4 randomized, controlled, open-label, parallel-group study of ENF added to oral HAART versus oral HAART alone in treatment-experienced patients with HIV. Enrollment was 47. ENF was administered by subcutaneous injection at 90 mg twice a day, with treatment planned for up to 48 weeks.

The primary endpoint was confirmed HIV-1 RNA < 50 copies/mL during induction, with response by Week 24 and confirmation at Week 28. The posted counts were 20.0 of 31.0 for ENF plus HAART and 8.0 of 16.0 for HAART. The risk difference, reported as HAART minus ENF plus HAART, was -0.145, with a 95% confidence interval from -0.443 to 0.152 and an unadjusted p-value of 0.337.

The numerical result favors ENF plus HAART, but the interval is wide and includes no difference. The registry record lists additional efficacy and safety outcomes but does not report a complete analysis plan, multiplicity strategy, or several details needed to assess missing data and phase-specific populations.