Switching From a Tenofovir Disoproxil Fumarate (TDF) Containing Regimen to Elvitegravir/Cobicistat/Emtricitabine/ Tenofovir Alafenamide (E/C/F/TAF) Fixed-Dose Combination (FDC) in Virologically-Suppressed, HIV-1 Infected Adults Aged ≥ 60 Years: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Switching From a Tenofovir Disoproxil Fumarate (TDF) Containing Regimen to Elvitegravir/Cobicistat/Emtricitabine/ Tenofovir Alafenamide (E/C/F/TAF) Fixed-Dose Combination (FDC) in Virologically-Suppressed, HIV-1 Infected Adults Aged ≥ 60 Years (NCT02616783), a randomized phase 3 study. The primary outcome is Percent Change From Baseline to Week 48 in Spine BMD.

2. Clinical Question

The registry record describes the study’s primary objective as evaluating safety relative to unchanged current antiretroviral therapy, using spine and hip bone mineral density at Week 48. The posted primary endpoint is specifically percent change in spine BMD. It is a continuous measurement, so the result concerns the average change in the analyzed groups rather than a count of participants crossing a threshold.

The clinical question is therefore narrower than whether the regimens differ in every aspect of HIV care or long-term health. The endpoint addresses a bone-density measure over the study’s reported follow-up. The study also listed HIV-1 RNA and CD4+ cell-count outcomes, but those are separate questions and should not be folded into the primary endpoint interpretation. Detailed results for several listed secondary outcomes are not reported in the registry record.

3. Trial Design

The registry identifies this as a Phase 3 study; its official title describes it as a Phase 3b randomized, open-label study. It used randomized allocation and a parallel-group model. Masking was listed as none, so the study was open label. The registry enrollment is 167 participants, while the primary endpoint analysis includes the participants with available data in the Spine DXA Analysis Set. These figures describe different things: enrollment is not the same as the analysis count for a particular outcome.

One group switched from a regimen containing TDF and FTC or 3TC plus a third agent to E/C/F/TAF. The other group remained on its current regimen, which could include TDF and FTC, FTC/TDF, or 3TC plus a continuing third agent. The described treatment period for the switching group was 48 weeks. The primary endpoint timeframe was baseline to Week 48.

The study status is completed. The registry record gives a start date of 2015-12-22 and a primary completion date of 2018-02-21. The sponsor is Gilead Sciences. The record does not report the randomization sequence-generation method, allocation concealment, details of site conduct, or whether any deviations from the assigned treatment occurred. It also does not report the original sample-size justification or the trial’s complete prespecified statistical analysis plan. Those details should not be inferred from the posted outcome results.

The parallel randomized comparison helps frame the results as between-group evidence, but the open-label design means participants and study personnel were not masked to group assignment. That feature is relevant when considering outcomes that may be affected by behavior, clinical decisions, or assessment procedures. BMD is an instrument-measured outcome, but the registry record does not give enough detail to assess measurement procedures or any safeguards beyond the stated analysis population.

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: 214 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in the Spine DXA Analysis Set with available data were analyzed.

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: Safety Analysis Set included all participants who were randomized into the study and received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percent Change From Baseline to Week 48 in Spine BMD, measured over Baseline; Week 48.

The primary endpoint is percent change from baseline to Week 48 in spine bone mineral density. BMD is a continuous measurement of bone mineral density, and percent change expresses the endpoint as a relative change from each participant’s baseline measurement. The registry describes the primary outcome as a mean with standard deviation and identifies the analysis population as participants in the Spine DXA Analysis Set with available data.

The registry’s primary objective places spine and hip BMD within a safety evaluation of switching from a TDF-containing regimen compared with remaining on the current antiretroviral therapy. The posted primary endpoint, however, is the spine measure; it should not be treated as a combined spine-and-hip outcome. Hip BMD was listed as a secondary endpoint at Week 24, and other secondary measures addressed spine BMD at Week 24, HIV-1 RNA, and CD4+ cell count.

Using a continuous BMD outcome retains information about the scale and direction of group-average change rather than reducing the measure to a binary category. A group mean describes the average outcome among analyzed participants; the standard deviation describes how much individual measurements vary around that average. Neither alone describes every participant’s response. The registry record does not state a clinically meaningful threshold for interpreting the size of a BMD change, nor does it report a rationale for selecting this specific endpoint beyond its role in the stated primary safety objective.

7. Results Posted in the Registry

• Stay on Baseline Regimen: mean -0.10 versus 2.24 on control; difference -2.34 (95% CI -3.44 to -1.24), standardized effect d = -0.71; z-test p = <0.001.

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.

Percent Change From Baseline to Week 24 in Spine BMD

• 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:
  • Stay on Baseline Regimen: mean -0.03 versus 1.62 on control; difference -1.65 (95% CI -2.66 to -0.64), standardized effect d = -0.52; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Stay on Baseline Regimen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent Change From Baseline to Week 24 in Hip BMD

• 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:
  • Stay on Baseline Regimen: mean -0.54 versus 0.81 on control; difference -1.35 (95% CI -2.17 to -0.52), standardized effect d = -0.60; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Stay on Baseline Regimen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 24 as Defined by the US FDA-Defined Snapshot Algorithm

• 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:
  • Stay on Baseline Regimen: 100.0% (55/55) versus 94.5% (103/109) on control; risk difference 5.5 percentage points (95% CI 1.2 to 9.8), risk ratio 1.06 (1.01–1.11); unadjusted two-proportion z-test p = 0.076.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stay on Baseline Regimen and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover spine and hip BMD, HIV-1 RNA suppression, and CD4+ cell count. Among the secondary results with numerical detail, the Week 24 BMD comparisons point in the same general direction as the primary Week 48 spine result: the reported group averages are higher in the switching group than in the group that remained on the baseline regimen. The Week 24 HIV-1 RNA result does not show the same clear statistical evidence of a between-group difference under the sponsor’s reported analysis.

This pattern is coherent with the primary BMD finding in the limited sense that the posted BMD results have a consistent direction across the reported timeframes and sites. It does not establish that all secondary outcomes follow that pattern, or that BMD findings determine the results for virologic or immunologic measures. Numerical results for several outcomes listed in the registry, including additional HIV-1 RNA and CD4+ cell-count outcomes, are not reported in the registry record.

Secondary analyses are usually interpreted more cautiously when many outcomes or timepoints are examined. Each additional comparison creates another opportunity for an apparently notable result to arise by chance. The registry record does not report whether the trial controlled the family of secondary tests for multiplicity, or how those outcomes were ranked in a prespecified analysis plan. Consequently, nominal p-values for secondary endpoints carry less weight than a result interpreted within a clearly reported multiplicity strategy. The secondary results can inform the overall pattern, but they should not be treated as independent confirmation of the primary endpoint.

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

• Percent Change From Baseline to Week 24 in Spine BMD
• Percent Change From Baseline to Week 24 in Hip BMD
• Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 24 as Defined by the US FDA-Defined Snapshot Algorithm
• Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 48 as Defined by the US FDA-Defined Snapshot Algorithm
• Change From Baseline in CD4+ Cell Count at Week 24
• Change in Baseline in CD4+ Cell Count at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has a measured percent change in spine BMD, and the registry reports group means and standard deviations. A mean describes the group’s average measurement. A standard deviation describes the spread of participant measurements around the mean. A larger standard deviation indicates more variability among individual measurements, not greater uncertainty about the treatment effect by itself. The uncertainty in a group comparison also depends on the number of participants analyzed and on the variability of the measurements.

What does the mean difference represent?

The re-calculation compares the two posted group means. Its reported comparison is ordered as the stay-on-baseline regimen group relative to E/C/F/TAF, giving an estimate of -2.341. Reversing the order of groups would reverse the sign, without changing the underlying contrast. This sign convention is why it is important to read the group labels and the means alongside a difference estimate. The re-calculation is a simple, unadjusted comparison based on posted summary statistics; it is not the sponsor’s model-based analysis.

The registry reports the sponsor’s primary analysis as ANOVA, with a difference in percentages, a confidence interval, and a p-value. ANOVA is a method for comparing group means under a statistical model. The record does not give enough detail to identify all terms in the model, adjustments, or assumptions used in that analysis. The reported analysis and the unadjusted re-calculation therefore describe related but distinct statistical summaries. Since the registry does not explain why their estimates differ, the methods and comparison directions should remain explicit when interpreting them.

How should a confidence interval be read?

A confidence interval communicates uncertainty around an estimated contrast. In repeated use under the method’s assumptions, confidence intervals at a stated level would contain the underlying value at the stated rate. For a single trial, the interval is not a guarantee that the true value lies inside it, and it is not a range containing a stated proportion of individual participants. The interval’s location relative to zero is useful for considering whether the data are compatible with no average difference, while its width indicates the precision of the estimate under the model.

The posted primary confidence interval for the simple re-calculation is from -3.445 to -1.237. The reported ANOVA interval is from 1.337 to 3.517. Their opposite signs reflect their stated comparison conventions. Both intervals exclude zero, but their estimates should not be combined or substituted for one another. The registry record does not report a multiplicity adjustment for these analyses.

What does a p-value say?

A p-value measures how compatible the observed data are with a statistical null hypothesis, given the chosen model and assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of effect size. For the primary endpoint, the reported analysis gives p < 0.001, and the simple re-calculation also gives p < 0.001. These values are evidence against the relevant null comparison under the respective analyses. They do not establish the importance of the difference to participants, resolve the open-label design, or account for unreported analysis decisions.

Statistical significance and clinical meaning are distinct. Whether a difference is important depends on context, measurement properties, and a meaningful threshold. The registry record does not report such a threshold for spine BMD. The group standard deviations also show that individual outcomes vary; a difference in group averages does not imply that every participant’s outcome matches the average pattern.

Why can over-dispersion matter?

General statistical explanation: for count outcomes, over-dispersion means that variability exceeds what a simple count model expects. Ignoring it can make uncertainty appear too small and confidence intervals too narrow. The primary outcome in this trial is a continuous BMD measure, not a count outcome, so over-dispersion is not the central issue for interpreting its mean comparison. The registry record does not report a special over-dispersion analysis.

For binary outcomes, such as whether HIV-1 RNA is below a stated threshold, the analysis concerns proportions rather than a continuous mean. Different methods can produce different estimates and intervals, especially when group sizes and observed proportions differ. The Week 24 HIV-1 RNA endpoint’s sponsor analysis is reported as Fisher Exact, while the primary BMD analysis is ANOVA. Their p-values and intervals answer different endpoint-specific questions and should not be compared as though they came from the same model.

General statistical explanation: randomization supports a between-group comparison by assigning participants to groups without selecting treatment based on measured or unmeasured characteristics, in expectation. It does not guarantee identical groups in a particular trial, and it cannot address missing outcomes or departures from the assigned treatment without further analysis. The registry record states that allocation was randomized but does not report the sequence generation, concealment, or detailed analysis population beyond the primary endpoint’s available-data Spine DXA set.

11. Confidence Intervals and Precision

The primary re-calculation reports a 95% confidence interval from -3.445 to -1.237 for the mean difference, ordered as stay on baseline regimen minus E/C/F/TAF. The sponsor-reported ANOVA analysis gives a 95% confidence interval from 1.337 to 3.517 for its difference in percentages. These intervals are both away from zero, but the signs and numerical estimates should be interpreted according to each analysis’s comparison convention and method. The registry record does not explain why the estimates differ.

In general, a confidence interval summarizes uncertainty in an estimated group contrast under the statistical method used. A narrower interval indicates greater precision for that estimate, while a wider interval indicates more uncertainty. The interval does not describe the range of outcomes among individual participants. The reported standard deviations, 3.273 for E/C/F/TAF and 3.385 for the baseline-regimen group, describe individual-level spread, a different concept from the precision of the estimated mean difference.

The available-data analysis population and the unequal numbers analyzed for the primary endpoint are relevant to precision. The record does not report a primary-endpoint missing-data sensitivity analysis, so the extent to which missing BMD data could affect the result is not quantified in the posted information. Confidence intervals also do not account for every possible source of uncertainty, including unreported model choices or bias associated with an open-label design.

For context, the Week 24 secondary BMD comparisons also have reported confidence intervals that exclude zero in their sponsor analyses. The Week 24 HIV-1 RNA sponsor interval includes zero for the difference in percentages. These intervals concern different outcomes and timeframes, and each should be interpreted using its own analysis method rather than as interchangeable measures of precision.

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 sample-size figures and curve are planning illustrations based on the observed effect, not the trial’s original design justification. For these continuous-outcome illustrations, the reported values are participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size assumptions or justification.

The 80% power column means the estimated number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column expresses the corresponding planning target at 90% power. These are hypothetical design calculations, not estimates of what the completed trial achieved. They are not observed power.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the planned effect size changes the sample-size requirement. Planning for a smaller effect requires more participants per arm to maintain the same target power, because a smaller group difference is harder to distinguish from variability. For example, the primary endpoint’s planning illustration gives 32 participants per arm for 80% power when using 100% of the observed effect, and 126 participants per arm when using 50% of that effect. These figures rely on the stated simplified assumptions and do not substitute for the trial’s unreported original planning rationale.

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 = -2.341; pooled standard deviation σ = 3.312.
2. n = 2 × (1.96 + 0.842)² × 3.312² / -2.341² = 31.4, rounded up to 32 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 <- -2.341                      # observed difference in means
sigma <- 3.31191919855048                     # 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(2616783)
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 = 32 (80% power), 43 (90% power)
 75% of observed effect: n per arm = 56 (80% power), 75 (90% power)
 50% of observed effect: n per arm = 126 (80% power), 169 (90% power)
power.t.test: 32.4 
Simulated power at n = 32 per arm: 0.797 (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 reports the sponsor’s primary endpoint analysis as ANOVA, with a difference in percentages of 2.427, a 95% confidence interval from 1.337 to 3.517, and p < 0.001. The posted re-calculation uses the group means and standard deviations to make a simple unadjusted comparison. Its difference is -2.341 when expressed as stay on baseline regimen minus E/C/F/TAF, with a 95% confidence interval from -3.445 to -1.237 and p < 0.001.

The directions are consistent once the comparison ordering is taken into account: the group means are 2.237 for E/C/F/TAF and -0.104 for the baseline regimen. The numerical estimates themselves are not the same. The sponsor analysis is identified as ANOVA, whereas the re-calculation is an unadjusted summary-statistic comparison. The registry record does not explain the difference in their estimates or provide enough detail to reproduce the sponsor’s model.

These analyses should therefore be read as distinct presentations of the primary comparison, not as competing numbers that can be averaged or directly substituted. The sponsor’s reported result is the registry’s stated analysis; the re-calculation helps describe a simple contrast from the posted group summaries. Neither should be interpreted without its method, direction convention, and analysis population.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes and reports analyses for more than one endpoint and timeframe. Testing multiple outcomes can increase the chance of at least one statistically notable result even when there is no underlying difference for any of them. Statistical methods that control multiplicity address this issue by adjusting inference or by setting a testing strategy in advance. The registry record does not report a multiplicity-control procedure, a hierarchy for testing endpoints, or a complete prespecified statistical analysis plan. It is therefore not possible to determine from the posted record whether or how multiplicity was handled.

The primary endpoint analysis population is described as participants in the Spine DXA Analysis Set with available data. This is important because the primary result is not explicitly described as including every randomized participant. The number enrolled and the numbers contributing to specific endpoint analyses are not identical concepts. The registry record does not report a detailed account of missing primary BMD measurements, reasons for missingness, imputation procedures, or sensitivity analyses that test the effect of missing data assumptions. The impact of missing BMD observations therefore cannot be assessed from the posted information.

The Week 24 HIV-1 RNA outcome is defined using the US FDA-Defined Snapshot Algorithm. That named outcome definition is reported, but it does not establish that the same missing-data approach was used for continuous BMD outcomes. The registry record does not provide enough information to reconstruct all outcome-specific analysis populations or handling rules for every secondary endpoint.

Randomization and the parallel-group design are reported, but details of the randomization process and allocation concealment are not. Masking is listed as none. The record also does not state whether all analyses followed assigned treatment, how treatment changes or protocol deviations were handled, or what adjustments were made in the sponsor’s ANOVA. Those omissions do not negate the posted results, but they limit independent evaluation of the analysis choices and the robustness of the conclusions.

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: acute coronary syndrome (1.8%), cardiac arrest (0.9%), cholecystitis acute (0.9%), escherichia sepsis (0.9%), pneumonia (0.9%).

The primary objective is described as a safety evaluation, and the registry provides serious adverse event counts and other adverse event counts for the two groups. Serious adverse events affected 10 of 110 participants in the E/C/F/TAF group and 1 of 56 participants in the group that stayed on the baseline regimen. Other adverse events affected 47 of 110 and 20 of 56 participants, respectively. The record reports 1 death in the E/C/F/TAF group and 0 in the baseline-regimen group.

The listed serious adverse event terms include acute coronary syndrome at 1.8%, and cardiac arrest, acute cholecystitis, Escherichia sepsis, pneumonia, and sepsis at 0.9% each. These are registry-listed terms and percentages; they do not establish that the events were caused by a study regimen. The record does not provide enough information in these figures alone to assess timing, event severity beyond the serious classification, relatedness, recurrent events, or participant-level clinical context.

Counts should be read with their stated group denominators and without treating them as a definitive causal comparison. Randomization can support group comparisons, but the safety figures do not by themselves establish a difference in risk, and the registry excerpt does not provide a formal comparative safety analysis. The figures also do not capture all possible risks or establish safety beyond the reported study period.

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

The posted primary result describes a difference in average change in spine BMD between the randomized groups among participants included in the available-data Spine DXA Analysis Set. The E/C/F/TAF group’s mean percent change was 2.237, while the group remaining on the baseline regimen had a mean percent change of -0.104. Both the sponsor-reported analysis and the simple unadjusted re-calculation indicate a between-group difference under their respective methods, with reported p-values below 0.001.

This result does not say that every participant’s BMD changed in the same direction as the group average. The standard deviations show variability in individual measurements. Nor does the result establish a clinically important threshold: the registry record does not report what magnitude of change should be considered meaningful. Statistical evidence against a null comparison is not a substitute for a clinical interpretation of the scale of the change.

The result is limited to spine BMD over the reported baseline-to-Week 48 period and the endpoint analysis population. It does not directly establish effects on hip BMD at Week 48, fractures, long-term outcomes, all aspects of safety, or virologic control. Those questions require their own outcomes and follow-up. The Week 24 secondary results offer additional information, but they do not change the definition of the primary endpoint or establish findings for outcomes whose numerical results are not reported.

The study’s randomized design supports a comparison between groups, while its open-label status and incomplete reporting of analysis details should be considered when judging how robustly the result can be interpreted. The registry record does not provide a detailed missing-data analysis, multiplicity strategy, or original sample-size rationale. These gaps limit assessment of the full analysis plan and the reach of the findings beyond the posted endpoint summary.

Accordingly, the result is best understood as evidence about the average measured spine BMD change in this study population and timeframe. It does not amount to a general claim about all older adults with HIV-1, all TDF-containing regimens, or long-term consequences. The posted results are specific to the groups and outcome definitions described in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint, analysis population, and comparison method matter when interpreting a clinical result. The primary question concerns a continuous measurement, so the average change and its variability are central. A group mean difference can show a clear statistical separation even when individual outcomes vary, and it does not reveal how many participants experienced a particular clinically important change unless such a threshold and analysis are reported.

The record also offers a useful distinction between the sponsor’s model-based analysis and a simple unadjusted re-calculation from group summaries. Both support a difference in the primary comparison under their stated methods, but their estimates are not identical. Preserving the comparison direction, method, and analysis population prevents readers from treating different statistical summaries as if they were the same estimand.

The secondary outcomes demonstrate another central biostatistical issue: several endpoints and timeframes can contribute context, but repeated testing raises multiplicity concerns. Without a reported multiplicity strategy, secondary p-values require caution, even when their directions appear consistent with the primary finding. Missing details about the original sample-size justification and missing-data sensitivity analyses further define what can and cannot be inferred.

Finally, the safety counts show why denominators, event definitions, and causal attribution must remain distinct. A registry event count is descriptive evidence; it does not by itself establish a regimen-related risk difference. Together, these features make the trial a useful example of reading a randomized comparison precisely while keeping statistical significance, estimation, clinical meaning, and limits of reporting separate.

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.

Several limitations specific to this trial can be identified from the registry record. The study was open label, with masking listed as none. That feature may be relevant to participant behavior, treatment decisions, and outcome assessment, although the primary BMD measurement is instrument-based. The registry record does not describe measurement procedures or provide enough detail to judge whether outcome assessment was insulated from knowledge of assignment.

The primary analysis used the Spine DXA Analysis Set with available data, rather than stating that every randomized participant contributed to the endpoint. The record does not report the reasons for unavailable measurements, the handling of missing primary endpoint data, or sensitivity analyses. This prevents assessment of whether missingness could alter the estimated comparison.

The sponsor’s ANOVA estimate and the simple re-calculation from group summaries are not numerically identical, and the registry record does not explain why. The record also does not provide the full model specification, original sample-size rationale, multiplicity strategy, or complete statistical analysis plan. These omissions constrain independent reproduction and evaluation of the reported analyses.

Generalizability is bounded by the population and regimens described: virologically suppressed adults aged ≥ 60 years with HIV-1 infection who were receiving TDF-containing therapy. The study reports a 48-week treatment period for the switching group and a primary endpoint at Week 48. The posted primary result should not be extended to other populations, regimens, outcomes, or longer follow-up without additional evidence. Several listed secondary outcomes lack numerical results in the registry record, limiting assessment of the full outcome pattern.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Switching From a Tenofovir Disoproxil Fumarate (TDF) Containing Regimen to Elvitegravir/Cobicistat/Emtricitabine/ Tenofovir Alafenamide (E/C/F/TAF) Fixed-Dose Combination (FDC) in Virologically-Suppressed, HIV-1 Infected Adults Aged ≥ 60 Years — NCT02616783.
• Registry record last updated 2020-03-04; status last verified 2019-01.
• Results first posted 2019-02-19.
• 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

The registry describes a completed Phase 3, randomized, open-label, parallel-group study of switching virologically suppressed adults aged ≥ 60 years with HIV-1 infection from a TDF-containing regimen to E/C/F/TAF, compared with remaining on the baseline regimen. Enrollment was 167. The primary endpoint was percent change from baseline to Week 48 in spine BMD among participants in the Spine DXA Analysis Set with available data.

The mean change was 2.237 for E/C/F/TAF and -0.104 for the baseline-regimen group. The sponsor-reported ANOVA analysis gave a difference in percentages of 2.427, with a 95% confidence interval from 1.337 to 3.517 and p < 0.001. The simple unadjusted re-calculation uses the opposite group ordering and reports -2.341, with a 95% confidence interval from -3.445 to -1.237 and p < 0.001. The record also lists secondary efficacy and safety outcomes, but does not report every analysis detail needed to assess missing data, multiplicity, or the full statistical plan.