KIVEXA Vs TRUVADA, Both Administered With Efavirenz, In ART-Naive Subjects: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for KIVEXA Vs TRUVADA, Both Administered With Efavirenz, In ART-Naive Subjects (NCT00549198), a randomized phase 4 study. The primary outcome is Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 48.

2. Clinical Question

The clinical question is comparative rather than a test of either regimen against no treatment: both groups received an active regimen with efavirenz. The trial therefore addresses whether the observed mean change in estimated GFR differed between the two treatment combinations over the stated follow-up period. It does not, by itself, answer every question about kidney function, other outcomes, longer-term toxicity, or regimen maintenance. The record describes the study as randomized and open-label, with a parallel-group model. Its primary endpoint was the MDRD estimate at Week 48; other renal measures and time points were also registered as secondary outcomes. The record does not report a formal equivalence or noninferiority objective, so a nonsignificant difference should not be interpreted as evidence that the regimens are equivalent.

3. Trial Design

This was a randomized, phase 4, parallel-group trial comparing abacavir/lamivudine and tenofovir/emtricitabine, with efavirenz administered in both groups. The title describes the participants as antiretroviral-naive, HIV-1 infected adult subjects. The registry record reports enrollment of 392 and lists HIV infection as the condition under study. The listed start and primary completion dates are 2007-06 and 2009-12, and the study status is completed.

The record identifies allocation as randomized and masking as none. Thus, the trial was open-label: participants and study personnel were not masked according to the registry designation. The model was parallel, meaning the record describes separate groups receiving the respective regimens rather than a crossover comparison. The listed phase is phase 4. The sponsor is GlaxoSmithKline.

The primary outcome was mean change from baseline in estimated GFR calculated using the MDRD equation at Week 48. The analysis population was defined as randomized participants who received at least one dose of study medication. The reported analysis method was Mixed Models Analysis, but further details about model specification, covariates, assumptions, or handling of observations are not reported in the registry record.

The record lists additional renal outcomes, including MDRD-based changes at Week 24 and Week 96, Cockcroft-Gault-based changes at several follow-up times, and counts of participants crossing specified thresholds of estimated GFR decline. It also lists 58 outcome measures and 20 analyses. The original sample-size justification, trial-specific power assumptions, and planned approach to interim analyses are not reported in the registry record. The distinction matters: planning illustrations based on the posted effect are not a description of the original trial design. The registry record supplies trial-level design labels and outcome definitions, but not enough protocol detail to reconstruct every operational or analytical decision.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat-Exposed (ITT-E) Population: all randomized participants who received at least one dose of study medication

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 Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 48, measured over Baseline, Week 48.

The primary endpoint is mean change from baseline to Week 48 in estimated glomerular filtration rate, calculated with the Modification of Diet in Renal Disease equation. GFR estimates the rate at which blood is filtered by the kidney. The MDRD equation uses serum creatinine, age, race, and gender to estimate GFR; it is described in the registry record as a validated estimate of renal function for participants with impaired renal function. The unit is mL/min/1.73 m^2.

Change was defined as the Week 48 value minus the baseline value. This makes the endpoint a within-participant change summarized as a group mean. A positive mean change indicates that the average estimated value at Week 48 was higher than baseline; a negative mean change indicates a lower average value. Such a change is an estimate based on a formula and is not a direct measurement of kidney filtration.

Using a continuous measure preserves information about the amount of change across the observed values, rather than reducing the result to whether a participant crossed a single threshold. That can be useful for comparing average trajectories between groups. It does not mean that a mean fully describes each participant’s experience or the distribution of changes. The registry record lists standard error as the dispersion statistic. The primary endpoint concerns renal function as estimated by MDRD at a specific follow-up time; it should not be treated as a measure of every aspect of kidney health or as a direct measure of clinical benefit.

7. Results Posted in the Registry

• TDF/FTC FDC: mean 1.18 versus 0.22 on control; difference 0.96 (95% CI -1.42 to 3.34), standardized effect d = 0.08; z-test p = 0.430.

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.

Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 24

• 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 errors.
• Result:
  • TDF/FTC FDC: mean 0.43 versus 2.78 on control; difference -2.35 (95% CI -4.74 to 0.04), standardized effect d = -0.20; z-test p = 0.054.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC FDC and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 96

• 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 errors.
• Result:
  • TDF/FTC FDC: mean -1.15 versus 1.48 on control; difference -2.63 (95% CI -5.36 to 0.10), standardized effect d = -0.19; z-test p = 0.059.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC FDC and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Estimated GFR, Calculated by Cockcroft-Gault Equation, at Week 24

• 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 errors.
• Result:
  • TDF/FTC FDC: mean 2.54 versus 4.27 on control; difference -1.73 (95% CI -4.28 to 0.82), standardized effect d = -0.14; z-test p = 0.184.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TDF/FTC FDC and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the renal comparison across other follow-up times and definitions. They include MDRD-based mean changes at Week 24 and Week 96, Cockcroft-Gault-based mean changes at specified follow-up times, and counts of participants meeting listed thresholds for decline in estimated GFR. Together, these measures provide related but not identical views of renal change: equations differ in how they estimate GFR, while continuous changes and threshold counts answer different questions.

The posted mean-change estimates show that the direction and size of group contrasts vary across measures and time points. The Week 24 and Week 96 MDRD comparisons have unadjusted recalculated p-values of 0.054 and 0.059, respectively, and their registry-reported mixed-model p-values are 0.057 and 0.060. The Cockcroft-Gault Week 24 comparison has an unadjusted recalculated p-value of 0.184 and a reported mixed-model p-value of 0.186. These secondary findings do not overturn or replace the primary Week 48 result; they add context about other registered renal measures and assessment times.

Secondary endpoints generally carry less weight for confirmatory conclusions when many outcomes or time points are examined without an established multiplicity strategy. Repeated testing increases the chance that some comparisons appear noteworthy by chance. The record lists 58 outcome measures and 20 analyses, but does not report a multiplicity adjustment or hierarchy for interpreting them. Therefore, unadjusted secondary results are best treated as exploratory or descriptive evidence, rather than as independent confirmation of a treatment difference.

The secondary outcomes also cannot be assumed to have been analyzed in the same way as the primary endpoint in every respect. The registry labels the reported analyses as Mixed Models Analysis, but detailed model specifications and analysis populations for each secondary comparison are not reported in the registry record. The appropriate overall reading is that the secondary outcomes offer additional, related evidence, while the primary endpoint remains the central registered comparison and the multiplicity context limits the strength of isolated secondary signals.

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

• Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 24
• Mean Change From Baseline in Estimated Glomerular Filtration Rate (GFR), Calculated by Modification of Diet in Renal Disease (MDRD) Equation, at Week 96
• Mean Change From Baseline in Estimated GFR, Calculated by Cockcroft-Gault Equation, at Week 24
• Mean Change From Baseline in Estimated GFR, Calculated by Cockcroft-Gault Equation, at Week 48
• Mean Change From Baseline in Estimated GFR, Calculated by Cockcroft-Gault Equation, at Week 96
• Number of Participants With Decline From Baseline in Estimated GFR, Calculated by MDRD and Cockcroft-Gault Equations, of >=10 mL/Min/1.73 m^2 (mL/Min for Cockcroft-Gault), >=20 mL/Min/1.72 m^2, >=10%, and >=20% at Week 24
• Number of Participants With Decline From Baseline in Estimated GFR, Calculated by MDRD and Cockcroft-Gault Equations, of >=10 mL/Min/1.73m^2 (mL/Min for Cockcroft-Gault), >=20 mL/Min/1.72m^2, >=10%, and >=20% at Week 48
• Number of Participants With Decline From Baseline in Estimated GFR, Calculated by MDRD and Cockcroft-Gault Equations, of >=10 mL/Min/1.73m^2 (mL/Min for Cockcroft-Gault), >=20 mL/Min/1.72m^2, >=10%, and >=20% at Week 96

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

The endpoint is continuous, and the posted group summaries are means with standard errors. The unadjusted comparison expresses the TDF/FTC FDC group mean minus the ABC/3TC FDC group mean. A positive estimate means the posted mean change was higher in the TDF/FTC FDC group; a negative estimate would mean it was lower. For the primary outcome, the recalculated estimate is 0.96 mL/min/1.73 m^2. This is a contrast between group averages, not a statement that every participant changed by that amount.

A mean difference is easy to interpret in the endpoint’s original measurement units. However, it can conceal variation between participants, including a range of individual changes that may not resemble the group average. The record reports standard errors for the group means. A standard error describes the estimated precision of a mean, rather than the spread of individual participant values. It is not interchangeable with a standard deviation.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimated contrast. In repeated use of the same method under its assumptions, intervals constructed in this way would cover the underlying parameter at the stated rate. For this primary comparison, the simple recalculated 95% confidence interval is -1.423 to 3.343 mL/min/1.73 m^2. Its inclusion of zero indicates that the unadjusted summary-statistic comparison does not clearly distinguish the estimated difference from no difference. The interval also indicates that values in either direction remain compatible with the calculation. It is not a guarantee that the true value lies within this particular interval.

The registry reports a Mixed Models Analysis with p = 0.435, but does not give the corresponding model-based effect estimate or confidence limits. The interval above is therefore not a reconstruction of the sponsor’s model. It is a simple unadjusted recalculation from the group summaries. The two approaches need not produce exactly the same result because a model-based analysis may use information and assumptions not represented by group means and standard errors alone. The model specification is not reported in the registry record.

Why can dispersion matter?

Variation among participants affects how precisely a group mean and a difference between means can be estimated. When data vary considerably, the mean difference can be uncertain even when the sample mean values look different. General statistical explanation: over-dispersion, when present relative to a model’s assumed variation, can make standard errors too small if it is not handled appropriately. That can make confidence intervals too narrow and p-values too small. The registry record does not report an over-dispersion assessment, so no conclusion about whether it arose in this trial can be made.

Here the posted dispersion values are standard errors, and the recalculation uses the summary statistics recorded for the groups. It does not add an adjustment for covariates or model features that are not documented. The reported Mixed Models Analysis is the trial’s stated method, but the available registry description does not establish precisely how repeated observations, missing measurements, or other sources of variation were treated.

How should the p-value be read?

The reported p-value of 0.435 is evidence from the sponsor’s stated analysis, interpreted under its model and the null hypothesis used by that analysis. It is not an effect size, a measure of clinical importance, or a probability that the null hypothesis is true. The unadjusted recalculation gives p = 0.43. Its proximity to the reported p-value is reassuring as a broad check on the posted summaries, but it does not make the methods identical. The registry record does not report a multiplicity adjustment or a detailed statistical analysis plan.

Statistical significance and clinical importance are different questions. A confidence interval can help assess the range of effects compatible with the data, while a judgment about importance requires a relevant clinical threshold. No such threshold for interpreting the primary endpoint is reported in the registry record. The study’s result should therefore be described in terms of its estimate, uncertainty, and analysis method, without converting the p-value into a claim that either regimen is better, worse, or equivalent.

What can and cannot be reconstructed?

The recalculated contrast is an unadjusted comparison of posted summary statistics. It is useful as a transparent check, but it cannot reproduce an analysis requiring participant-level observations or undocumented model choices. The registry record identifies the analysis as a mixed model, yet details such as model terms, covariance structure, treatment of missing data, and any planned sensitivity analyses are not reported in the registry record. Consequently, interpretation should give priority to the trial’s reported analysis while treating the recalculation as a separate descriptive aid. Neither summary can supply information about outcomes or design decisions that were not recorded.

11. Confidence Intervals and Precision

The primary mean difference is 0.96 mL/min/1.73 m^2 for TDF/FTC FDC compared with ABC/3TC FDC. The unadjusted recalculated 95% confidence interval extends from -1.423 to 3.343 mL/min/1.73 m^2. The interval spans zero and includes estimates in both directions. Thus the posted summary statistics do not pin down the direction of the underlying difference with high precision. The interval also makes clear that a range of effect sizes remains compatible with the recalculation; the point estimate alone would give an incomplete account of uncertainty.

A confidence interval is not a range containing a fixed proportion of individual participant outcomes. It describes uncertainty about a group-level contrast under the method used to construct it. Nor does inclusion of zero prove that there is no difference. It indicates that zero is among the values not ruled out by this interval at its stated confidence level. The registry-reported mixed-model p-value is 0.435, but the registry record does not report a model-based confidence interval for that analysis. The recalculated interval should therefore be read as an unadjusted summary-statistic interval, not as a confidence interval from the sponsor’s model.

Precision is distinct from clinical importance. The registry record does not report a threshold that would define a clinically important difference in MDRD-estimated GFR. Without such a threshold, the interval can describe statistical uncertainty but cannot classify all compatible values as important or unimportant. It also concerns the average change at Week 48, rather than every participant’s response or later renal outcomes. These limitations make it important to keep the estimate, its interval, the analysis method, and the clinical context in view together.

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 this continuous outcome; they are not total event counts. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses a stated fraction of the observed effect as the effect to detect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm in a hypothetical design that would have an 80% chance of detecting the specified effect, if the calculation’s assumptions hold. The 90% power column describes a hypothetical design with a higher chance of detecting that same effect under those assumptions. These are planning illustrations based on the observed effect, not observed power. Observed power is not an informative substitute for interpreting the estimate and its uncertainty after a trial has been completed.

The rows correspond to planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to achieve the same nominal power in this calculation. The figures should not be read as evidence that the original trial was designed around these effect fractions or that its design used these assumptions. They do not change the result of the completed trial, and they do not show what the observed analysis would have produced under a different sample size. Their role is to illustrate how assumptions about the target effect and desired power influence planning.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.960; pooled standard deviation σ = 11.924.
2. n = 2 × (1.96 + 0.842)² × 11.924² / 0.960² = 2,421.7, rounded up to 2,422 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
delta <- 0.96                      # observed difference in means
sigma <- 11.9237012915815                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(549198)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 2,422 (80% power), 3,242 (90% power)
 75% of observed effect: n per arm = 4,306 (80% power), 5,764 (90% power)
 50% of observed effect: n per arm = 9,687 (80% power), 12,968 (90% power)
power.t.test: 2422.6 
Simulated power at n = 2,422 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry record reports a Mixed Models Analysis for the primary comparison, with p = 0.435. It does not provide the model-based treatment contrast or its confidence interval. The posted group means and standard errors allow a simple unadjusted recalculation: the estimated mean difference for TDF/FTC FDC compared with ABC/3TC FDC is 0.96 mL/min/1.73 m^2, with a 95% confidence interval of -1.423 to 3.343 and p = 0.43.

The recalculated p-value is close to the reported model-based p-value, but the figures arise from different analyses. The recalculation uses only posted summary statistics and does not account for unreported model terms, participant-level data, or assumptions. The registry result is the sponsor’s stated analysis and takes precedence as the trial’s reported inferential result; the recalculation is a supplementary check, not a replacement. Since the discrepancy flag is false, no specific disagreement requiring resolution is identified in the record.

The numerical agreement should not be overstated as proof that the analyses are interchangeable. The sponsor’s analysis is identified as a mixed model, while the recalculation is unadjusted. Details needed to reproduce or audit the model fully are not reported in the registry record. Readers should therefore distinguish the reported p-value from the independently recalculated estimate and interval, and should not attribute the recalculated interval to the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 58 outcome measures and 20 analyses. It does not report how the trial controlled the chance of false-positive findings across multiple outcomes, follow-up times, or analyses. No multiplicity adjustment, testing hierarchy, or prespecified family of outcomes is reported in the registry record. This matters because repeatedly testing many hypotheses can make at least one result appear unusual even when no underlying effect exists. Unadjusted secondary p-values should consequently be interpreted cautiously and should not be treated as if each were the sole planned test.

The primary outcome is identified, but the record does not give a detailed statistical analysis plan explaining how the primary and secondary tests were ordered or whether any outcomes were intended to be confirmatory. It also does not report interim analyses or stopping rules. These items cannot be inferred from the trial’s phase or completion status.

The record defines the primary analysis population as randomized participants who received at least one dose of study medication. That definition differs from an unrestricted all-randomized population, but the record does not explain whether anyone randomized did not receive medication or how such cases were handled. For the endpoint, the available summaries show group denominators, but do not explain the availability of Week 48 measurements or how missing values were treated in the mixed model. The registry record does not report the extent, reasons, or pattern of missing outcome data, nor does it describe imputation or sensitivity analyses.

These omissions limit assessment of how robust the results are to missingness and how fully the reported analysis followed the planned approach. A mixed-model label alone does not establish the assumptions made about incomplete repeated measurements or the precise model specification. The result remains interpretable as the reported analysis, but the record does not permit a complete evaluation of multiplicity control, missing-data handling, or all analysis-population decisions.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: drug hypersensitivity (2.6%), pneumonia (2.6%), hypersensitivity (1.6%), gastroenteritis (1.0%), immune reconstitution syndrome (1.0%).

The serious adverse event figures count participants with at least one serious adverse event in each listed group. The registry reports 31 affected among 192 at risk in the ABC/3TC FDC group and 20 among 193 at risk in the TDF/FTC FDC group. These are counts, not event rates per unit of follow-up, and the record does not provide a comparative statistical analysis for them. They should not be interpreted as establishing a causal difference between regimens.

The listed serious adverse event terms include Drug hypersensitivity and Pneumonia, each reported as 2.6%; Hypersensitivity at 1.6%; Gastroenteritis and Immune reconstitution syndrome, each at 1.0%; and Lower respiratory tract infection at 0.5%. These are the terms and percentages identified among the top serious terms in the record. The presentation does not establish that each term occurred in both groups or give group-specific counts for every listed term.

The record does not report deaths for these groups. Serious adverse event counts do not summarize all adverse events, their duration, severity beyond the serious classification, or the overall balance of benefits and harms. They provide descriptive safety information and should be read separately from the primary renal endpoint.

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

The result describes a comparison of mean change in MDRD-estimated GFR from baseline to Week 48 in participants who were randomized and received at least one dose of study medication. The posted means were 0.22 mL/min/1.73 m^2 for ABC/3TC FDC and 1.18 mL/min/1.73 m^2 for TDF/FTC FDC. The unadjusted recalculated difference was 0.96 mL/min/1.73 m^2, with a 95% confidence interval of -1.423 to 3.343. The registry-reported mixed-model p-value was 0.435.

These data do not provide strong statistical evidence of a difference in the primary endpoint under the reported analysis. They also do not prove that the regimens have identical effects. The confidence interval includes zero and a range of differences in either direction; the record supplies no clinical threshold for deciding which values would matter clinically. The result therefore does not establish equivalence, noninferiority, or absence of a clinically important difference.

The endpoint is an equation-based estimate of renal filtration, not a direct measurement of every dimension of kidney health. It is also a group mean at a defined follow-up time. It cannot show that every participant experienced a change matching the average, nor does it by itself address other clinical outcomes, treatment adherence, regimen maintenance, or long-term toxicity. The record’s additional renal outcomes add context, but multiplicity and incomplete analysis details limit how strongly isolated secondary findings can be interpreted.

Likewise, the serious adverse event counts are descriptive and do not establish that one regimen is safer. A full judgment about the treatment options would require consideration of clinical outcomes and harms beyond this primary endpoint, along with trial details not reported in the registry record. The appropriate conclusion is limited: the posted primary comparison is imprecise enough to include no difference and effects in either direction, and the record does not justify a broader claim about overall treatment superiority or equivalence.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places a direct randomized comparison around a continuous renal-function estimate in participants starting an antiretroviral regimen. Both arms included efavirenz, so the comparison concerns the two fixed-dose combination components within the regimens described, rather than a contrast between treatment and no treatment. The primary endpoint and follow-up time are explicitly identified, allowing the estimate to be interpreted in a defined clinical and statistical context.

The result also illustrates why the estimate, interval, and analysis method should be considered together. The point estimate is positive, but its unadjusted 95% confidence interval spans zero and the registry-reported mixed-model p-value is 0.435. A point estimate alone could overstate certainty; a p-value alone would conceal the range of compatible effects. The parallel reporting of group summaries and a sponsor-reported model analysis also highlights that a recalculation from summary data is not necessarily identical to the trial’s analysis.

There is additional statistical value in seeing outcomes defined using more than one GFR equation and across multiple follow-up times. Those outcomes may illuminate consistency or variation in the observed pattern, but they also create a multiplicity challenge. Since an adjustment strategy is not reported, secondary findings require restraint rather than selective emphasis.

Finally, the registry record documents limitations that matter for reproducibility: it identifies a mixed-model method but not its detailed specification, and it does not report missing-data handling, multiplicity control, or the original sample-size justification. These gaps do not erase the reported findings, but they limit how far an independent reader can audit the analysis or infer what was prespecified. The trial is a useful example of separating a descriptive contrast from confirmatory inference and of avoiding claims that exceed the precision and documentation available.

19. Limitations

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

The registry record does not provide the model-based primary effect estimate or confidence interval, only the Mixed Models Analysis label and p-value. This prevents direct comparison of the model estimate with the unadjusted recalculation and limits independent review of the primary analysis. Model details such as covariates, repeated-measures structure, covariance assumptions, and sensitivity analyses are not reported in the registry record.

Missing outcome data are another uncertainty. The record does not report the amount, timing, or reasons for missing Week 48 measurements, or how such missingness was addressed. Although the analysis population is defined as randomized participants who received at least one dose, the record does not detail the relationship between that population and the participants contributing data at each follow-up time.

The record lists many outcome measures and analyses, but does not report a multiplicity plan or testing hierarchy. This limits confirmatory interpretation of secondary results. It also does not report the trial’s original sample-size rationale, so planning illustrations based on the observed effect cannot be used to judge whether the study was designed to detect a prespecified clinically important difference.

The design was open-label according to the masking designation. The primary endpoint is an equation-based estimate rather than a direct measurement, and the registry does not report a clinical-importance threshold for interpreting its change. Serious adverse event counts are descriptive; comparative safety analyses and deaths are not reported in the record. These limitations constrain claims about the size, clinical meaning, and broader treatment implications of the observed differences.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: KIVEXA Vs TRUVADA, Both Administered With Efavirenz, In ART-Naive Subjects — NCT00549198.
• Registry record last updated 2011-04-12; status last verified 2011-04.
• Results first posted 2010-10-15.
• 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

NCT00549198 is a completed, randomized, open-label, parallel-group phase 4 trial of abacavir/lamivudine versus tenofovir/emtricitabine, both administered with efavirenz, in antiretroviral-naive adults with HIV-1 infection. The registry record reports enrollment of 392 and identifies mean change from baseline to Week 48 in MDRD-estimated GFR as the primary endpoint.

The posted group means were 0.22 mL/min/1.73 m^2 for ABC/3TC FDC and 1.18 mL/min/1.73 m^2 for TDF/FTC FDC. The unadjusted recalculated mean difference was 0.96, with a 95% confidence interval of -1.423 to 3.343; the registry-reported mixed-model p-value was 0.435. The interval includes zero, and the record does not establish equivalence or noninferiority.

Secondary renal outcomes provide additional time points and measures, while multiplicity, missing-data handling, and detailed model specifications are not reported in the registry record. Serious adverse event counts are descriptive and do not constitute a comparative safety analysis.