Entecavir Plus Adefovir Combination Therapy Versus Entecavir Monotherapy vs Therapy With Adefovir Plus Lamivudine for Chronic Hepatitis B Infected Subjects With Lamivudine-resistant Virus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Entecavir Plus Adefovir Combination Therapy Versus Entecavir Monotherapy vs Therapy With Adefovir Plus Lamivudine for Chronic Hepatitis B Infected Subjects With Lamivudine-resistant Virus (NCT00410202), a randomized phase 3 study. The primary outcome is Percentage of Participants With Hepatitis B Virus (HBV) Deoxyribonucleic Acid (DNA) < 50 IU/mL (Approximately 300 Copies/mL) by Polymerase Chain Reaction (PCR) at Week 48.

2. Clinical Question

The primary outcome is a laboratory-defined threshold response, not a direct measure of symptoms, liver complications, or long-term health. It captures whether a participant’s HBV DNA level was below the stated threshold at a specified assessment. The registry describes missing efficacy assessments as failures, so the percentage reflects both measured responses and the stated handling of missing assessments.

The clinical question has two contrasts, each against the combination of entecavir and adefovir. The trial does not directly compare entecavir monotherapy with adefovir plus lamivudine in the sponsor-reported primary analyses. The registry record does not report a hypothesis about which regimen should have the greatest response, nor does it describe a clinical threshold for a meaningful difference between groups.

3. Trial Design

The DEFINE study was a phase 3 randomized trial with a parallel-group design and no masking. It enrolled participants with chronic hepatitis B and lamivudine-resistant virus. The registry lists an enrollment of 629 and marks the study completed. The recorded start was 2008-03, and primary completion was 2011-01.

Participants were assigned to entecavir plus adefovir, entecavir monotherapy, or adefovir plus lamivudine. The registry describes an option to add tenofovir at week 48 for the entecavir monotherapy group, except in Korea. The record does not report how many participants used this option, how treatment changes were handled in the analyses, or whether the option applied before or after the primary assessment for each participant. These details should not be inferred from the arm description alone.

The primary endpoint was the percentage of participants with HBV DNA below 50 IU/mL at week 48, assessed using the Roche COBAS TaqMan High Pure System assay. The primary population was participants who received at least one dose of study therapy. Missing efficacy assessments were classified as failures. The registry also lists 24 secondary outcomes among 25 outcome measures, covering further HBV DNA thresholds and categories, other assessment weeks, and change in mean log10 HBV DNA from baseline.

The registry record does not report the original sample-size justification, the planned primary analysis model, the randomization procedure, allocation concealment, or details of any interim analyses. It also does not report the duration of follow-up for the safety summaries. The presence of a randomized, open-label, parallel design describes important features of the trial, but it does not fill in these unreported methods.

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: Of the 629 participants enrolled, 416 were randomized (195 no longer met study criteria, 9 withdrew consent, and 9 had other reason). One participant randomized to entecavir + adefovir (ADV+LVD) Arm withdrew consent before treatment.

On-Treatment

Reasons for not completing this period:

Off-treatment Follow up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants who received at least 1 dose of study therapy. Participants with missing efficacy assessments were considered as a failure.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Hepatitis B Virus (HBV) Deoxyribonucleic Acid (DNA) < 50 IU/mL (Approximately 300 Copies/mL) by Polymerase Chain Reaction (PCR) at Week 48, measured over Week 48.

The primary endpoint is the percentage of participants whose HBV DNA was below 50 IU/mL at week 48, measured by polymerase chain reaction. The registry gives the assay-specific equivalent as approximately 300 copies/mL. This is a binary outcome: each participant is classified according to whether the measured value is below the cutoff at the assessment. The reported percentage is based on the number meeting the threshold relative to the number analyzed, with missing efficacy assessments counted as failures.

A threshold endpoint can be useful because it gives a clinically interpretable summary of how many participants reach a specified laboratory level at a particular time. It also makes a comparison between randomized groups straightforward. However, it does not preserve all information about the measured HBV DNA values: participants on either side of the cutoff are placed into different categories even if their underlying values are close, while differing values on the same side of the cutoff receive the same endpoint classification.

This endpoint is specific to week 48 and the stated assay threshold. It does not by itself describe the size of each participant’s change from baseline, persistence of the response, or outcomes beyond the assessment. Those questions require other outcomes and follow-up information. The registry lists additional threshold outcomes at week 48 and week 96, but the primary question remains the proportion below 50 IU/mL at week 48.

The registry record does not report a clinical rationale for selecting this particular cutoff or a minimum difference between groups that would be considered important. Statistical evidence about a group contrast therefore should not be treated as a complete judgment about its clinical importance.

7. Results Posted in the Registry

• ETV Monotherapy: 16.4% (23/140) versus 25.4% (35/138) on control; risk difference -8.9 percentage points (95% CI -18.4 to 0.6), risk ratio 0.65 (0.40–1.04); unadjusted two-proportion z-test p = 0.067.
• ADV+LVD Combination Therapy: 19.7% (27/137) versus 25.4% (35/138) on control; risk difference -5.7 percentage points (95% CI -15.5 to 4.2), risk ratio 0.78 (0.50–1.21); unadjusted two-proportion z-test p = 0.262.

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.

Percentage of Participants With HBV DNA < 50 IU/mL (Approximately 300 Copies/mL) by PCR at Week 96

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ETV Monotherapy: 39.3% (55/140) versus 43.5% (60/138) on control; risk difference -4.2 percentage points (95% CI -15.8 to 7.4), risk ratio 0.90 (0.68–1.20); unadjusted two-proportion z-test p = 0.478.
  • ADV+LVD Combination Therapy: 28.5% (39/137) versus 43.5% (60/138) on control; risk difference -15.0 percentage points (95% CI -26.2 to -3.8), risk ratio 0.65 (0.47–0.91); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ETV Monotherapy and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for ADV+LVD Combination Therapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Achieve HBV DNA < Lower Limit of Quantitation (LOQ = 29 IU/mL [Approximately 169 Copies/mL]) at Week 48

• 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:
  • ETV Monotherapy: 13.6% (19/140) versus 25.4% (35/138) on control; risk difference -11.8 percentage points (95% CI -21.0 to -2.6), risk ratio 0.54 (0.32–0.89); unadjusted two-proportion z-test p = 0.013.
  • ADV+LVD Combination Therapy: 16.8% (23/137) versus 25.4% (35/138) on control; risk difference -8.6 percentage points (95% CI -18.2 to 1.0), risk ratio 0.66 (0.41–1.06); unadjusted two-proportion z-test p = 0.081.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for ETV Monotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ADV+LVD Combination Therapy and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Achieve HBV DNA < Lower Limit of Quantitation (LOQ = 29 IU/mL [Approximately 169 Copies/mL]) at Week 96

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ETV Monotherapy: 36.4% (51/140) versus 38.4% (53/138) on control; risk difference -2.0 percentage points (95% CI -13.4 to 9.4), risk ratio 0.95 (0.70–1.29); unadjusted two-proportion z-test p = 0.733.
  • ADV+LVD Combination Therapy: 25.5% (35/137) versus 38.4% (53/138) on control; risk difference -12.9 percentage points (95% CI -23.8 to -1.9), risk ratio 0.67 (0.47–0.95); unadjusted two-proportion z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ETV Monotherapy and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for ADV+LVD Combination Therapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question across additional HBV DNA thresholds, assessment times, categories, and a change-from-baseline measure. The posted results show that patterns can differ by threshold and assessment week; a finding for one definition or time point should not be assumed to apply to another. In particular, the endpoint based on less than 50 IU/mL at week 96 has reported arm percentages of 43.5%, 39.3%, and 28.5% for entecavir plus adefovir, entecavir monotherapy, and adefovir plus lamivudine, respectively. Other secondary threshold outcomes are also listed in the registry.

These analyses provide context for the week 48 primary outcome, but they do not replace it. They ask related but distinct questions: whether a different threshold is met, whether the threshold response is observed at another week, or how the distribution or average change is characterized. Their results should be interpreted on their own definitions and time frames rather than as repeated measurements of a single identical claim.

There are many secondary outcomes and analyses in the registry. If multiple comparisons are examined, some results may appear statistically notable by chance, especially when no adjustment is made. The record identifies a Hochberg procedure for the primary comparisons, but it does not report a comprehensive multiplicity plan for all secondary outcomes. Unadjusted secondary results therefore carry less inferential weight than a prespecified, appropriately controlled primary analysis. They can be informative and hypothesis-generating, but should not be presented as independent confirmation without considering the number of tests and the analysis plan.

The registry reports a significant adjusted comparison for the week 96 less-than-50-IU/mL outcome between entecavir plus adefovir and adefovir plus lamivudine: difference estimate 15.0, 95% confidence interval 3.7 to 26.4, p = 0.009. This is a secondary result at a different assessment week; it does not alter the interpretation of the primary week 48 comparisons. Other secondary outcomes and their exact analyses should be distinguished from that finding rather than pooled into a broad conclusion.

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

• Percentage of Participants With HBV DNA < 50 IU/mL (Approximately 300 Copies/mL) by PCR at Week 96
• Percentage of Participants Who Achieve HBV DNA < Lower Limit of Quantitation (LOQ = 29 IU/mL [Approximately 169 Copies/mL]) at Week 48
• Percentage of Participants Who Achieve HBV DNA < Lower Limit of Quantitation (LOQ = 29 IU/mL [Approximately 169 Copies/mL]) at Week 96
• Percentage of Participants Who Achieve HBV DNA < Lower Limit of Detection (LOD = 10 IU/mL [Approximately 58 Copies/mL]) at Week 48
• Percentage of Participants Who Achieve HBV DNA < Lower Limit of Detection (LOD = 10 IU/mL [Approximately 58 Copies/mL]) at Week 96
• Percentage of Participants With HBV DNA by PCR Category at Week 48
• Percentage of Participants With HBV DNA by PCR Category at Week 96
• Change in Mean log10 From Baseline in HBV DNA at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion with an outcome in one group with the proportion in another. A value of zero represents equal proportions; values on either side indicate which group has the greater observed proportion, depending on the order of subtraction. In the recalculated comparisons, the entecavir plus adefovir group is the reference and the other group is subtracted from it. Thus, a negative estimate corresponds to a lower observed response proportion in the comparison group. The sponsor reports its difference estimates in the opposite descriptive direction for these contrasts, so the signs should not be compared without attending to the stated group order.

A risk difference is an absolute contrast on the probability scale. It answers how far apart the proportions are, rather than how many times as large one is relative to the other. The arm percentages and the reported difference estimates are different summaries of the same broad comparison. The latter is useful because it gives an estimated group contrast and an uncertainty interval.

What does a confidence interval add?

A confidence interval expresses the uncertainty around an estimate under the assumptions of the analysis. It gives a range of values compatible with the observed data and the specified method; it is not a guarantee that the true effect lies within that particular interval. When an interval for a difference includes zero, the data do not rule out no difference at the confidence level used. The interval may also include contrasts favoring either group, which is why a single point estimate should not be read as a precise answer.

The sponsor’s primary 95% intervals include zero for both comparisons. This is consistent with the adjusted p-values not meeting a conventional threshold for statistical significance. The recalculated intervals are unadjusted and should not be used to override the sponsor’s multiplicity-adjusted analyses. A p-value measures how unusual the observed data would be under a specified null model; it is not the probability that the null hypothesis is true, nor is it a measure of clinical importance.

Why distinguish adjusted and unadjusted analyses?

When several hypotheses are tested, the chance of at least one apparently notable result can increase. A multiplicity procedure adjusts inference across a defined family of comparisons. The registry identifies the Hochberg procedure for the reported primary comparisons. The recalculations use simple, unadjusted comparisons from the posted summary counts, so they do not account for that family of tests. They are useful as a transparent check on the scale of the contrasts, but the sponsor’s own analysis is the relevant reported primary analysis.

Multiplicity adjustment does not change the underlying observed percentages. It changes how the statistical evidence is assessed across comparisons. The registry record does not report the full testing hierarchy, the complete family of hypotheses covered by each adjustment, or whether the secondary analyses were adjusted. Those unknowns limit any broader claim about control of false-positive findings.

What is the analysis population?

The primary endpoint description defines the population as participants who received at least one dose of study therapy. It further states that missing efficacy assessments were considered failures. This is not enough information to label the analysis as a particular standard population, such as intention-to-treat, without additional details. The registry record does not report the precise participant flow, the count of missing assessments, or sensitivity analyses using alternative missing-data assumptions.

Counting missing assessments as failures makes the endpoint classification conservative in the sense that missing participants do not contribute a successful threshold response. It does not eliminate possible bias: if missingness differs between groups or is related to unobserved outcomes, the resulting group proportions may still be affected. The amount and reasons for missingness are not reported in the registry record.

What does randomization contribute, and what does it not guarantee?

Random assignment is intended to make the comparison groups similar, on average, with respect to measured and unmeasured baseline characteristics. It supports a causal interpretation of differences in outcomes when the assigned groups are analyzed appropriately. The registry states that allocation was randomized, but details of sequence generation, concealment, adherence, and post-randomization treatment changes are not reported. The stated option to add tenofovir in the entecavir monotherapy group is therefore relevant context, but the registry record does not describe its use or analytic handling.

The study was open-label, meaning masking was not used. Knowledge of treatment assignment can affect care and participant behavior, and can influence assessments that involve judgment. The primary endpoint is based on an assay, which is less dependent on subjective rating than some outcomes, but open-label status remains part of the design context. No details about blinded laboratory assessment are reported.

How should the binary endpoint be understood?

A binary threshold outcome simplifies a continuous laboratory measurement into whether a stated cutoff was reached. This can make results easier to communicate, but it discards information about the distance from the cutoff and the amount of change from baseline. A separate outcome such as change in mean log10 HBV DNA addresses a different question. The registry lists such an outcome, but its results are not included in the registry record for this analysis.

General statistical principles help explain these choices, but they cannot fill in missing trial-specific methods. In particular, the registry record does not report the original sample-size justification, a prespecified clinically important difference, the planned model for the primary endpoint, or details of interim monitoring. Interpretation should therefore focus on the recorded design, the posted endpoint results, and the uncertainty represented by the reported intervals.

11. Confidence Intervals and Precision

The precision of a group comparison is conveyed most directly by its confidence interval. For the primary comparison with entecavir monotherapy, the sponsor’s difference estimate was 8.9, with a 95% interval from -2.0 to 19.9. For the comparison with adefovir plus lamivudine, the estimate was 5.7, with a 95% interval from -4.2 to 15.5. Both intervals include zero and span values on either side of no difference. The point estimates alone therefore do not capture the range of effects compatible with the data.

The recalculated unadjusted intervals likewise extend across zero: -0.184 to 0.006 for the monotherapy comparison and -0.155 to 0.042 for the adefovir plus lamivudine comparison. These intervals arise from simple unadjusted re-calculations and are not the sponsor’s multiplicity-adjusted results. Their signs use the opposite comparison order from the sponsor’s difference estimates.

In general, a wider interval indicates less precision, while a narrower interval indicates greater precision under the analysis assumptions. Precision depends on the amount of information and the variability of the outcome. For a binary endpoint, the number of participants and the response proportions contribute to uncertainty. The posted primary intervals leave room for both little or no difference and potentially larger contrasts, so the estimates should not be treated as exact rankings.

Confidence intervals describe statistical uncertainty, not all sources of uncertainty. They do not account automatically for open-label conduct, missing outcome assessments, treatment changes, or the choice of endpoint and analysis. The registry does not report enough detail to quantify those influences. Nor does an interval identify whether a difference is clinically important; the registry record does not report a meaningful-difference threshold.

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 are planning illustrations based on the observed effect, not the original trial’s design calculation. For these binary outcomes, the figures refer to participants per arm. The listed 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 as the stated fraction of the observed effect. The original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm that would, under those assumptions, give an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities conditional on the assumed effect and model; they are not probabilities that the trial result is correct.

Rows planning for smaller fractions of the observed effect require more participants per arm. This is expected: a smaller difference is harder to distinguish from random variation, all else held constant. The planning figures are illustrations rather than a recommendation for a future study, since the original effect may not repeat and the registry does not report a clinically important target difference. The sample-size figures are not observed power.

The plotted planning curve should be read as a visual expression of the same assumptions and effect scenarios, not as an additional analysis of the trial’s actual design. It does not establish what the trial was originally powered to detect. For outcomes involving time to event, the stated convention would be total events; that convention does not apply to these binary percentage outcomes.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.254; treatment proportion p₁ = 0.164; average p̄ = 0.209.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5750 = 1.1269.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5715 = 0.4810.
4. n = (1.1269 + 0.4810)² / (-0.0893)² = 323.9, rounded up to 324 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 <- 0.253623188405797                          # control proportion
p1 <- 0.164285714285714                          # 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(410202)
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 = 324 (80% power), 434 (90% power)
 75% of observed effect: n per arm = 600 (80% power), 802 (90% power)
 50% of observed effect: n per arm = 1,398 (80% power), 1,871 (90% power)
power.prop.test: 323.9 
Simulated power at n = 324 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor-reported primary analyses compare entecavir plus adefovir with each of the other groups using a Hochberg procedure. Against entecavir monotherapy, the reported difference estimate is 8.9, with a 95% confidence interval from -2.0 to 19.9 and p = 0.134. Against adefovir plus lamivudine, the reported estimate is 5.7, with a 95% confidence interval from -4.2 to 15.5 and p = 0.262.

The recalculated contrasts are simple, unadjusted calculations from the posted event counts and group sizes. They express each comparison group relative to entecavir plus adefovir, so their negative estimates have the reverse sign from the sponsor’s difference estimates. The recalculated p-values are 0.067 and 0.262, respectively, and the recalculated confidence intervals are unadjusted.

The registry identifies no discrepancy between the posted counts and sponsor analyses. Even so, the sponsor’s own analysis takes precedence for interpretation of the primary comparisons because it is the reported analysis and includes the stated Hochberg procedure. The recalculations are best treated as a check on the direction and approximate scale of the contrasts, not as replacement inferential results. Neither set of primary results gives conclusive evidence of a difference at the conventional significance threshold.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity. The primary outcome includes two comparisons against entecavir plus adefovir. The registry reports that the sponsor used the Hochberg procedure for these primary analyses. This method adjusts inference across multiple tests, reducing the risk of interpreting one chance finding as persuasive evidence when more than one comparison is made. The posted p-values for the primary contrasts are therefore adjusted results. The registry record does not state the full hypothesis hierarchy or how multiplicity was handled across all secondary endpoints and analyses.

The recalculated p-values are unadjusted. They should not be read as the sponsor’s final inferential results or compared with adjusted p-values as if they were produced by the same procedure. The registry lists 25 outcome measures and 24 analyses, which makes the distinction between primary and secondary evidence important. The record does not report whether all secondary analyses were prespecified or whether any adjustment was applied to them.

Missing data. The primary endpoint description states that participants with missing efficacy assessments were considered failures. This clarifies the classification rule but does not reveal how many assessments were missing, why they were missing, or whether missingness differed across groups. The registry record does not report sensitivity analyses under alternative missing-data assumptions. Consequently, the robustness of the primary result to missingness cannot be assessed from the recorded information.

Analysis populations. The stated primary population consists of participants who received at least one dose of study therapy. The record does not provide enough detail to determine whether this is identical to a named analysis population used in the full trial report. It also does not describe exclusions after randomization, protocol deviations, or the handling of treatment changes in detail. Those omissions matter because the population analyzed and the treatment strategy represented can affect interpretation of a randomized comparison. The endpoint and analysis-population descriptions should therefore be retained when describing what the posted results estimate.

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: hepatic neoplasm malignant (3.6%), haemorrhoids (2.1%), intervertebral disc protrusion (1.4%), appendicitis (1.4%), oesophageal varices haemorrhage (0.7%).

The registry reports serious adverse events for each treatment group, using group-specific numbers at risk and numbers affected. The entries are 14 of 138 for entecavir plus adefovir, 21 of 140 for entecavir monotherapy, and 13 of 137 for adefovir plus lamivudine. These are counts of participants with serious adverse events, not counts of all individual serious events. The record also lists other adverse events: 63 of 138, 75 of 140, and 62 of 137, respectively. The registry does not specify in the registry record whether the “other” category excludes serious events or how categories overlap.

The listed serious-event terms include hepatic neoplasm malignant at 3.6%, haemorrhoids at 2.1%, intervertebral disc protrusion at 1.4%, appendicitis at 1.4%, oesophageal varices haemorrhage at 0.7%, and intracranial hypotension at 0.7%. The record does not give group-specific rates for these terms in the registry record, so they should not be assigned to a particular treatment arm.

These figures are descriptive. They do not establish that treatment caused an event or that one regimen is safer than another. The registry does not report comparative safety estimates, confidence intervals, or deaths for these groups in the listed details. Follow-up duration and detailed event-collection methods are also not reported in the registry record.

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

The central finding is a comparison of the proportions reaching a laboratory threshold at week 48. The posted percentages are numerically higher for entecavir plus adefovir than for either comparison group. However, the sponsor-reported primary confidence intervals include no difference, and the Hochberg-adjusted p-values do not provide statistically conclusive evidence of a group difference. The estimates remain uncertain, and the interval ranges allow more than one interpretation of the underlying contrast.

This does not mean the regimens are equivalent. A failure to establish a difference is not proof that two treatments have the same effect. Equivalence or non-inferiority claims require a defined margin and an analysis designed for that purpose; such a margin is not reported in the registry record. Nor does the observed ordering of percentages establish that one regimen is better in a broader clinical sense.

The endpoint is a week 48 laboratory response below 50 IU/mL, with missing assessments counted as failures in the stated primary population. It does not directly establish an effect on symptoms, liver complications, survival, or outcomes beyond the measured assessment. Other outcomes may address different questions, but they should not be substituted for the primary endpoint.

Statistical uncertainty is only one part of interpretation. The open-label design, the option to add tenofovir in the entecavir monotherapy group at week 48 except in Korea, and unreported details about missingness and treatment changes are relevant context. The record does not provide enough information to quantify how those features affected results. No treatment recommendation follows from these statistical comparisons; interpretation should stay within the population, endpoint, assessment time, and analysis reported.

18. Why This Trial Matters Statistically

This trial illustrates why a numerical difference between group percentages and a statistically conclusive result are not the same thing. The entecavir plus adefovir group has the highest posted percentage for the primary threshold outcome, but the sponsor’s uncertainty intervals span zero for both primary comparisons. Reporting the estimate together with its interval and adjusted p-value gives a more complete account than ranking groups by their percentages alone.

It also demonstrates the importance of specifying the direction of a contrast. The sponsor’s difference estimates are expressed in a different direction from the simple recalculated risk differences. Without checking which group is subtracted from which, the sign can be misread as indicating the opposite treatment pattern. The arm percentages help anchor the direction, while the stated contrast and analysis method explain how inferential results were obtained.

The trial’s multiple endpoints raise another general statistical issue: the more outcomes and comparisons examined, the more important it is to distinguish a designated primary analysis from secondary findings. The reported Hochberg procedure addresses the primary comparisons, while the registry record does not provide a complete multiplicity plan for all secondary results. This affects how strongly secondary p-values should be interpreted.

Finally, the stated missing-data rule is part of the outcome definition in practice. Counting a missing assessment as failure is transparent, but the effect of that rule cannot be evaluated without information on how much data were missing and why. Together, these features make the trial useful for understanding the interplay of endpoint definition, contrast direction, multiplicity, and precision in clinical trial interpretation.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations affect what can be concluded from the registry record. The study was open-label, and the record does not describe whether laboratory personnel were masked to treatment assignment. The endpoint is an objective laboratory threshold, but the absence of masking remains relevant to trial conduct and the interpretation of other outcomes.

The entecavir monotherapy arm included an option to add tenofovir at week 48, except in Korea. The registry does not report how many participants took this option, the timing of any changes, or how they were handled analytically. This limits the ability to characterize the treatment contrast fully at and after that time point.

The primary endpoint dichotomizes HBV DNA at a specified threshold and assessment time. It does not capture the full continuous distribution or long-term persistence of response. The registry record does not report a clinically important difference threshold, the original sample-size justification, or the planned primary statistical model. It also does not report the amount and pattern of missing efficacy assessments, despite specifying that missing assessments counted as failures.

The record lists numerous secondary outcomes, but a full plan for multiplicity across those outcomes is not reported. Details of allocation concealment, the randomization process, adherence, participant flow, protocol deviations, and sensitivity analyses are also not reported in the registry record. Safety follow-up duration and group-specific serious-event term rates are not available in the listed details. These omissions do not invalidate the posted results, but they constrain assessment of bias, robustness, and generalizability beyond the described trial population and endpoint.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Entecavir Plus Adefovir Combination Therapy Versus Entecavir Monotherapy vs Therapy With Adefovir Plus Lamivudine for Chronic Hepatitis B Infected Subjects With Lamivudine-resistant Virus — NCT00410202.
• Registry record last updated 2013-11-21; status last verified 2013-10.
• Results first posted 2012-07-04.
• 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

DEFINE was a completed phase 3 randomized, open-label, parallel-group study of participants with lamivudine-resistant chronic hepatitis B. It compared entecavir plus adefovir with entecavir monotherapy and adefovir plus lamivudine. The primary outcome was the percentage with HBV DNA below 50 IU/mL at week 48; missing efficacy assessments were counted as failures in the population that received at least one dose of study therapy.

The posted primary percentages were 25.4%, 16.4%, and 19.7%, respectively. The sponsor-reported Hochberg-adjusted comparisons had 95% confidence intervals that included zero. These results do not establish a primary-endpoint difference, while also not establishing equivalence. Secondary outcomes address additional thresholds and assessment times, and require interpretation with attention to multiplicity. The registry record does not report the original sample-size justification, complete secondary multiplicity plan, or several details needed to assess missingness and treatment changes.