Entecavir Plus Tenofovir Combination Therapy Versus Entecavir Monotherapy in Naive Subjects With Chronic Hepatitis B: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Entecavir Plus Tenofovir Combination Therapy Versus Entecavir Monotherapy in Naive Subjects With Chronic Hepatitis B (NCT00410072), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved Hepatitis B Virus DNA (HBV DNA) Levels <50 IU/mL by Polymerase Chain Reaction (PCR) at Week 96.

2. Clinical Question

The clinical question is whether the percentage of treatment-naive adults with chronic hepatitis B who achieve HBV DNA levels <50 IU/mL by PCR at Week 96 differs between entecavir plus tenofovir combination therapy and entecavir monotherapy. The registry also describes safety as a study aim. The primary endpoint captures a virologic response at a specified follow-up visit; it does not by itself describe every aspect of hepatitis B disease or patient experience.

3. Trial Design

This was a Phase 3, randomized, parallel-group study of two drug regimens. The registry lists 669 participants enrolled. One group received entecavir 0.5 mg, and the other received entecavir 0.5 mg plus tenofovir 300 mg. The study was open-label, meaning masking was listed as none. The study began in 2007-04, had primary completion in 2010-10, and is listed as completed.

The study’s stated purpose was to compare the effectiveness of the combination regimen with entecavir monotherapy, with safety also to be studied. Its primary outcome was the percentage of participants reaching HBV DNA levels <50 IU/mL by PCR at Week 96. The registry describes the threshold as approximately 300 copies/mL. Other listed outcomes include virologic measures at Weeks 48 and 96, mean log 10 HBV DNA, ALT normalization, HBeAg loss and seroconversion, and HBsAg loss.

Randomization supports a comparison between assigned groups, but the registry record does not report the sequence-generation method, allocation concealment, or any other procedural details. The record also does not report the original sample-size justification or the planned statistical analysis in enough detail to reconstruct the full protocol. The posted primary analysis population is described as evaluable participants, with missing efficacy assessments counted as failures. This is important when interpreting the group percentages: the denominator and handling of incomplete observations are part of the outcome definition, not merely a display choice.

The posted primary endpoint results include 182 participants in the entecavir group and 197 in the combination group. These endpoint denominators are not the same as the overall enrollment figure, and the record’s endpoint description specifies that participants who received treatment were included in the denominator for binary efficacy analyses. The exact accounting of all enrolled participants across treatment, follow-up, and analysis populations is not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 669 participants were enrolled; 384 were randomized. Among 285 who were not randomized, 266 did not meet the study criteria, 11 other, 1 poor compliance/noncompliance, 4 lost to follow-up, 1 withdrew consent, and 2 for administrative reasons.

Day 1 to Week 48

Reasons for not completing this period:

After Week 48 to Week 96

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Evaluable participants. A participant missing the efficacy assessments for a visit is considered a failure and is counted as evaluable.

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 Percentage of Participants Who Achieved Hepatitis B Virus DNA (HBV DNA) Levels <50 IU/mL by Polymerase Chain Reaction (PCR) at Week 96, measured over At Week 96.

The primary endpoint is the percentage of participants who achieved HBV DNA levels <50 IU/mL by PCR at Week 96. HBV DNA is a measure of viral genetic material in blood; using a prespecified threshold turns the measurement into a binary response, with each participant counted as either meeting or not meeting the endpoint. The registry states that <50 IU/mL is approximately 300 copies/mL.

A threshold-based endpoint makes the treatment groups’ response proportions directly comparable at a defined time point. It can be clinically and scientifically useful for summarizing virologic suppression, while remaining narrower than a complete account of disease status, long-term outcomes, or safety. A participant just above the threshold and one with a much higher measurement are both classified as nonresponders for this endpoint, although their underlying measurements differ.

The registry describes the binary efficacy analysis as on-treatment and says missing measurements were handled with noncompleter=failure. All participants who received treatment were included in the denominator, and a missing assessment counted as a nonresponse for that endpoint. Thus, the posted percentage reflects both observed endpoint values and this explicit missing-data rule. The registry identifies the primary population as evaluable participants and states that a participant missing efficacy assessments for a visit is considered a failure and counted as evaluable.

7. Results Posted in the Registry

• ETV 0.5 mg +TDF 300 mg: 83.2% (164/197) versus 76.4% (139/182) on control; risk difference 6.9 percentage points (95% CI -1.2 to 15.0), risk ratio 1.09 (0.98–1.21); unadjusted two-proportion z-test p = 0.095.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either achieved the specified HBV DNA threshold at Week 96 or did not. For a binary outcome, a group percentage describes the observed proportion meeting the response definition. Comparing these proportions is one way to summarize the difference between treatment groups. The registry’s primary result is expressed as a percentage, while the sponsor-reported comparison is described as a mean difference in final values and analyzed with a Cochran-Mantel-Haenszel method.

What the reported comparison describes

The Cochran-Mantel-Haenszel method is generally used to compare groups while accounting for strata. The registry record identifies the method but does not describe the strata, adjustments, or detailed model specification used in this analysis. It is therefore appropriate to report the named method and its result, but not to infer which covariates or stratification variables were included. The registry reports a mean difference in final values of 6.9, with a 95% confidence interval from -1.0 to 14.9 and p=0.088.

The simple recalculation is different in scope: it is an unadjusted comparison of the posted summary statistics. Its risk difference estimate is 0.069, with an interval from -0.012 to 0.149 and p=0.095. In general, a risk difference expresses the difference between two response proportions on the probability scale. The recalculated estimate should be understood as a check based on the posted counts, not as a substitute for an analysis that may account for features of the trial design or analysis population.

Why the distinction between analyses matters

Different statistical procedures can target related but not identical quantities or use different assumptions. An adjusted or stratified analysis can differ from a crude comparison because it incorporates information beyond the overall group totals. The registry does not report enough detail to fully explain every difference between its analysis and a simple recalculation. The reported sponsor analysis should therefore remain the principal analysis to interpret, while the unadjusted calculation offers a transparent supplementary view of the posted summary data.

For either approach, uncertainty is conveyed by an interval around the estimate and by the p-value. In general, a confidence interval describes a range of estimates compatible with the data and the method’s assumptions. It is not a range containing a fixed percentage of individual participant outcomes, and it does not assign a probability to the truth of a particular treatment effect. A p-value measures how unusual data at least as extreme as those observed would be under a specified null hypothesis and model; it does not measure the magnitude or importance of an effect.

How missing outcomes enter the analysis

The registry describes the binary efficacy analyses as on-treatment and states that they used noncompleter=failure. All participants who received treatment were included in the denominator, and participants with missing measurements were counted as nonresponders for the specific endpoint. This rule is explicit and affects the interpretation of the response percentages. It is not the same as assuming that missing outcomes would have matched the observed outcomes, nor does it recover the unknown measurements. The record does not report alternative missing-data analyses or sensitivity analyses, so the robustness of the finding to other missing-data assumptions cannot be assessed from the registry entry.

The primary population is called evaluable participants. The registry further says a participant missing efficacy assessments for a visit is considered a failure and counted as evaluable. That description links the analysis population to the endpoint-specific failure rule. Details about other analysis populations, such as a complete-case population or an all-randomized analysis, are not reported in the registry record. The record also does not provide the number of missing primary endpoint assessments by arm.

Why over-dispersion can matter in general

For binary data, a simple model may assume that outcomes vary only according to the response probability and the number of participants. In general, over-dispersion means the observed variability is greater than that simple model expects. If it is present and not accounted for, standard errors and confidence intervals may be too narrow, and tests may be too optimistic. The registry record does not report an over-dispersion assessment or a model that requires such an adjustment; this is a general statistical consideration, not a claim about this trial.

Multiplicity and interpretation

Testing multiple outcomes, time points, or comparisons increases the opportunity for chance findings. In general, multiplicity procedures control the overall error rate or otherwise structure interpretation across a family of tests. The registry lists multiple outcomes and analyses, but does not report a multiplicity adjustment or a prespecified hierarchy for them. The primary endpoint can be distinguished by its designation in the record, but the status of secondary findings should be interpreted with care because the complete analysis plan is not reported.

Finally, the trial was randomized but unmasked. Randomization is generally intended to reduce systematic differences in treatment assignment, while lack of masking can influence behavior, assessment, or decisions in some settings. The endpoint is a laboratory-based threshold, but the record does not report procedures for laboratory masking or other safeguards. These general considerations do not establish that bias occurred; they identify details that cannot be resolved from the registry record.

10. Confidence Intervals and Precision

The sponsor-reported estimate is 6.9, with a 95% confidence interval from -1.0 to 14.9. Because the interval includes zero, the data do not rule out no difference under this analysis. The interval also extends to estimates on either side of zero, so it does not tightly determine the direction or size of the group difference. Its width conveys appreciable uncertainty around the point estimate.

The unadjusted recalculation gives a risk difference of 0.069, with an interval from -0.012 to 0.149. This interval also includes zero and permits a range of possible group differences. It is based on the posted summary counts and should not be conflated with the sponsor’s Cochran-Mantel-Haenszel result. Both intervals lead to a similar broad reading: the estimated difference is positive, but its precision is insufficient to establish a clear difference.

In general, a confidence interval reflects both the observed data and the method’s assumptions. It is not a guarantee that the true effect lies within its endpoints, and it does not show the distribution of individual responses. Precision depends in part on the amount of information available and the variability of the data. The registry record does not report a prespecified equivalence margin, so the intervals cannot be used to claim that the treatments are sufficiently similar. Nor does the interval alone determine clinical importance; that requires context and a defined threshold for an important difference, neither of which is specified in the registry record.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the original trial design. For this binary outcome, the entries are participants per arm, rather than total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities under assumptions, not guarantees about a future study and not a measure of how likely the observed result is to be true.

The rows consider planning for 100%, 75%, and 50% of the observed effect. The listed participant counts rise as the assumed effect becomes smaller: for 100% of the observed effect, the estimates are 534 participants per arm for 80% power and 715 participants per arm for 90% power; for 75%, they are 980 and 1,312; and for 50%, they are 2,272 and 3,041. Smaller effects need more participants to distinguish them from random variation under the same planning assumptions. These values are not observed power; they are sample-size planning illustrations derived from the observed effect, not evidence about the probability that the completed study detected a true effect.

12. 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 = 0.764; treatment proportion p₁ = 0.832; average p̄ = 0.798.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5677 = 1.1126.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5656 = 0.4760.
4. n = (1.1126 + 0.4760)² / (0.0688)² = 533.9, rounded up to 534 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 <- 0.763736263736264                          # control proportion
p1 <- 0.83248730964467                          # 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(410072)
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 = 534 (80% power), 715 (90% power)
 75% of observed effect: n per arm = 980 (80% power), 1,312 (90% power)
 50% of observed effect: n per arm = 2,272 (80% power), 3,041 (90% power)
power.prop.test: 533.9 
Simulated power at n = 534 per arm: 0.803 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s own analysis as a Cochran-Mantel-Haenszel comparison of mean difference in final values. The estimate is 6.9, with a 95% confidence interval from -1.0 to 14.9 and p=0.088. That analysis is the principal registry-reported result and should be distinguished from the simple unadjusted recalculation.

The recalculation uses the posted group counts and gives a risk difference of 0.069, with an interval from -0.012 to 0.149 and p=0.095. It is a straightforward unadjusted analysis of summary statistics, not a reconstruction of every feature of the sponsor’s method. The registry does not report enough detail about strata or adjustments to make the two analyses identical. Their numerical results differ, but both have intervals that include zero and both indicate uncertainty about the size and direction of the group difference.

The registry record does not flag a discrepancy between the results. The recalculation is therefore best read as a supplementary check, not a correction of the sponsor’s analysis. Neither result should be interpreted as proving equivalence, and neither p-value describes the probability that a treatment effect exists.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 16 outcome measures, 15 secondary outcomes posted, and 19 analyses. Secondary measures cover additional virologic thresholds and time points, mean log 10 HBV DNA, ALT normalization, HBeAg outcomes, and HBsAg loss. Considering many outcomes and analyses raises a multiplicity question: in general, the more hypotheses examined, the greater the chance that at least one result will appear notable by chance alone.

The registry record does not report whether multiplicity was controlled, which outcomes formed a testing family, whether a hierarchy was prespecified, or whether secondary analyses were exploratory. The primary endpoint is identified, but the analysis plan for interpreting the wider set of results is not reported in the registry record. Secondary findings should therefore not be treated as confirmatory solely because they appear among posted analyses.

For the primary binary endpoint, missing measurements were counted as failures using noncompleter=failure. The registry says all participants who received treatment were included in the denominator and that participants with missing measurements were counted as nonresponders for the specific endpoint. It also defines an evaluable participant with a missing efficacy assessment for a visit as a failure counted as evaluable. This makes the missing-data rule part of the estimand being described: the reported response percentage combines observed responses with the prespecified classification of missing observations as failures.

The number of missing primary assessments by treatment group, reasons for missingness, and results under alternative assumptions are not reported in the registry record. Nor are sensitivity analyses that would show whether conclusions change under other plausible approaches. The original protocol’s analysis populations and handling rules beyond the posted description are not reported. These gaps limit assessment of how dependent the result is on the missing-data convention, but they do not justify assuming that a different convention would change the finding.

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: hepatic neoplasm malignant (1.6%), traumatic brain injury (1.0%), acute psychosis (0.5%), ovarian cyst (0.5%), cerebral ischaemia (0.5%).

The registry reports serious adverse events affecting 13 of 182 participants in the entecavir 0.5 mg group and 14 of 197 participants in the entecavir 0.5 mg plus tenofovir group. Other adverse events affected 69 of 182 and 73 of 197 participants, respectively. These are descriptive counts of participants affected, not estimates of treatment-attributable risk. The record does not establish from these figures whether any event was caused by a study drug.

The listed serious adverse event terms include hepatic neoplasm malignant at 1.6%, traumatic brain injury at 1.0%, acute psychosis at 0.5%, ovarian cyst at 0.5%, cerebral ischaemia at 0.5%, and cerebrovascular accident at 0.5%. These entries are event terms and percentages, not a complete account of all safety outcomes. The registry record does not report death counts. It also does not provide enough detail in these figures to assess event timing, severity beyond the serious classification, exposure-adjusted rates, or comparative uncertainty. Differences in raw counts alone should not be read as evidence of a safety advantage or disadvantage.

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

The posted primary endpoint results show that 76.4 of participants in the entecavir group and 83.2 in the combination group achieved HBV DNA levels <50 IU/mL by PCR at Week 96. The sponsor-reported comparison estimates a difference of 6.9, with a 95% confidence interval from -1.0 to 14.9 and p=0.088. The simple unadjusted recalculation likewise has an interval that includes zero. These findings describe the observed groups and the uncertainty around their comparison; they do not establish a clear difference under the reported analyses.

The result also does not establish that the regimens are equivalent. A failure to show a statistically clear difference is not the same as demonstrating that any difference is small enough to be unimportant. Equivalence or noninferiority requires a prespecified margin and an analysis designed for that question; such a margin is not reported in the registry record. Conversely, the positive point estimate alone is not proof that combination therapy produces a larger response in the population.

The primary endpoint is a threshold-based measure at Week 96. It does not on its own characterize sustained response beyond that visit, other clinical outcomes, or the full balance of benefits and harms. The posted secondary outcomes broaden the scope of measurement, but their multiplicity plan is not reported. Safety counts are descriptive, and the record does not report deaths in the adverse event summary.

Overall, the registry supports a cautious reading: the combination group had the higher observed response percentage, while the reported uncertainty leaves the comparative effect unresolved. Interpretation depends on the endpoint definition, the noncompleter=failure rule, and the statistical analysis used. These data should not be turned into individual treatment advice or a claim of benefit or lack of benefit.

17. Why This Trial Matters Statistically

This trial illustrates why a group difference should be read together with its uncertainty. The observed response percentages are not the entire result: the sponsor’s confidence interval includes zero, and the p-value is 0.088. A point estimate alone can make a comparison look more definite than the data allow. Intervals show that a range of effects remains compatible with the observations under the analysis assumptions.

It also demonstrates the importance of distinguishing a sponsor-reported analysis from a simple unadjusted recalculation. Both use the same trial context but differ in method and reported effect measure. A recalculation can provide a transparent check of summary counts, yet it cannot reproduce undocumented stratification or adjustments. Treating the methods as interchangeable could obscure what the registry analysis actually tested.

The handling of missing outcomes is another central statistical feature. Counting missing assessments as failures makes the endpoint definition explicit and affects the resulting percentages. Without the number and pattern of missing assessments, or sensitivity analyses under alternative assumptions, readers cannot fully assess how robust the comparison is to missingness.

Finally, the registry lists multiple outcomes and analyses without reporting a multiplicity plan. This matters because evidence from secondary endpoints requires a framework for interpreting the collection of tests, not just each result in isolation. Together, these features show why clinical trial interpretation requires attention to estimand, analysis method, missing data, multiplicity, and precision—not only the direction of a percentage difference.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the detailed randomization procedure, allocation concealment, or the original sample-size justification. It identifies the trial as randomized and open-label, but does not give enough information to assess all protections against selection or assessment bias. The lack of masking may be relevant to some outcomes and trial processes; the record does not describe whether laboratory assessments or other procedures were masked.

The primary outcome is a binary threshold at a single stated follow-up time. Such a summary does not show the full distribution of HBV DNA values, and participants on opposite sides of the threshold may have measurements close to one another. The endpoint does not encompass every clinical outcome or long-term consequence. The record lists other outcomes, but the full statistical plan and multiplicity approach are not reported.

The primary analysis uses noncompleter=failure. The number of missing measurements by arm, reasons for missingness, and sensitivity analyses are not reported in the registry record. As a result, the effect of alternative missing-data assumptions cannot be evaluated from the posted information. The exact details of the reported Cochran-Mantel-Haenszel analysis, including any strata or adjustments, are also not reported.

The primary result has appreciable uncertainty, with the sponsor-reported confidence interval including zero. The registry does not report an equivalence or noninferiority margin, so the comparison cannot establish that the regimens are equivalent. Safety findings are limited in the posted summary: event counts are descriptive, causal attribution is not established by the counts, and deaths are not reported in the registry record. These limitations define what can be concluded from the registry information; they do not establish that bias or harm occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Entecavir Plus Tenofovir Combination Therapy Versus Entecavir Monotherapy in Naive Subjects With Chronic Hepatitis B — NCT00410072.
• Registry record last updated 2013-03-15; status last verified 2013-03.
• Results first posted 2012-02-03.
• 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 BE-LOW study was a completed Phase 3 randomized, open-label, parallel-group comparison in adults with chronic hepatitis B who were treatment-naive to nucleosides and nucleotides. The registry lists 669 participants enrolled and a study period from 2007-04 to primary completion in 2010-10. It compared entecavir 0.5 mg with entecavir 0.5 mg plus tenofovir 300 mg.

The primary endpoint was achievement of HBV DNA levels <50 IU/mL by PCR at Week 96. The posted response percentages were 76.4 and 83.2, respectively. The sponsor-reported difference was 6.9, with a 95% confidence interval from -1.0 to 14.9 and p=0.088. The registry describes missing efficacy measurements as failures. The record also posts secondary outcomes and adverse event counts, but does not report a multiplicity plan, the original sample-size justification, or death counts.