Comparing Safety and Immunogenicity of HEPLISAV-B® to Engerix-B® in Chronic Kidney Disease (CKD) Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing Safety and Immunogenicity of HEPLISAV-B® to Engerix-B® in Chronic Kidney Disease (CKD) Patients (NCT00985426), a randomized phase 3 study. The primary outcome is Seroprotection Rate (SPR) = Percentage of Participants Who Have a Seroprotective Immune Response.

2. Clinical Question

This is an immunogenicity question: the endpoint records whether participants crossed a specified antibody threshold. It does not directly measure prevention of hepatitis B infection or another clinical outcome. The registry also lists safety outcomes and additional immunogenicity assessments over time. Those outcomes add context, but they do not change the meaning of the primary week 28 comparison.

3. Trial Design

The registry describes a completed phase 3, randomized, double-masked, parallel-group study sponsored by Dynavax Technologies Corporation. The reported enrollment was 521. The record lists chronic kidney disease as the condition and describes the study as comparing the safety and immunogenicity of HEPLISAV-B with licensed vaccine Engerix-B among adults aged 18 to 75 years.

Participants were assigned to HEPLISAV-B or Engerix-B. The HEPLISAV-B arm description includes both HEPLISAV-B and placebo injections, while the Engerix-B arm description lists Engerix-B. The registry identifies the study as double-masked but does not report the masking procedures. The record lists a study start of 2009-09 and primary completion of 2012-01.

The primary endpoint was the seroprotection rate at week 28. Its analysis population was modified intent-to-treat, defined in the registry as randomized participants who received at least one study injection and had at least one post-injection immunogenicity evaluation. The registry reports 227 participants in the HEPLISAV-B primary analysis group and 242 in the Engerix-B group. These are endpoint analysis denominators, not a restatement of total enrollment.

The registry also lists post-injection local and systemic reactions, seroprotection at other assessment weeks, antibody concentrations, and seroprotection among participants with type 2 diabetes mellitus. The original design’s sample-size assumptions, allocation ratio, and detailed statistical plan are not reported in the registry record. The posted planning illustration is based on the observed effect and should not be read as documentation of the study’s original design.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat (mITT) population comprises all randomized participants who received at least 1 study injection and had at least 1 post-injection immunogenicity evaluation.

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 population includes randomized participants who received at least 1 study injection.

6. Primary Endpoint

The registry lists the primary outcome as Seroprotection Rate (SPR) = Percentage of Participants Who Have a Seroprotective Immune Response, measured over Week 28.

The primary endpoint is the seroprotection rate at week 28: the percentage of participants whose anti-HBsAg antibody level was greater than or equal to 10 mIU/mL. In the primary analysis, the registry records 204 participants with seroprotection among 227 in the HEPLISAV-B group, and 198 among 242 in the Engerix-B group.

This is a binary endpoint. Each participant is classified according to whether the antibody threshold was reached, and the group result is expressed as a proportion or percentage. A threshold-based endpoint gives a direct way to compare the share of participants meeting a defined immunogenicity criterion. It does not preserve all information about the underlying antibody concentration: participants just below and far below the threshold are both classified as not meeting it, while participants at different levels above the threshold are counted as meeting it.

As a general statistical point, binary endpoints are useful when the research question concerns the probability of reaching a prespecified state. The threshold and assessment time define what is being compared. Here, the endpoint concerns antibody response at week 28, not the duration of protection, infection incidence, or clinical outcomes. The registry reports additional antibody assessments at other weeks, but those do not replace the specified primary time point.

7. Results Posted in the Registry

• Engerix-B: 81.8% (198/242) versus 89.9% (204/227) on control; risk difference -8.0 percentage points (95% CI -14.3 to -1.8), risk ratio 0.91 (0.85–0.98); unadjusted two-proportion z-test p = 0.013.

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.

SPR of Participants With Type 2 Diabetes Mellitus at Week 28

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Engerix-B: 76.7% (115/150) versus 89.5% (137/153) on control; risk difference -12.9 percentage points (95% CI -21.2 to -4.5), risk ratio 0.86 (0.77–0.95); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Engerix-B than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary assessments of post-injection local and systemic reactions, seroprotection over multiple assessment weeks, antibody levels, and seroprotection among participants with type 2 diabetes mellitus. A secondary analysis for the diabetes subgroup is posted at week 28 and is labelled superiority. Across the immunogenicity outcomes, the registry presents evidence that is broadly aligned with the primary comparison’s direction, while the outcomes differ in population, assessment time, or measurement scale.

Secondary outcomes help describe whether the primary finding appears in a subgroup or at other assessment times, and whether results are also considered using antibody levels rather than a threshold. They do not establish that every secondary measure has the same interpretation or evidential strength as the primary endpoint. Each outcome has its own analysis population and uncertainty, and subgroup findings apply only to the subgroup described.

Unadjusted secondary results carry less weight when many outcomes or assessment times are considered. As a general statistical point, testing multiple hypotheses increases the chance that at least one result appears noteworthy by chance, unless the analysis plan addresses multiplicity. The registry’s adjustment strategy and prespecified hierarchy are not reported, so the listed secondary findings should be treated as supportive and exploratory rather than as independent confirmation of the primary result. The secondary analyses do not change the definition or analysis population of the primary week 28 endpoint.

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

• Reactogenicity as Measured by the Percentage of Participants With Local and Systemic Post-injection Reactions Within 7 Days After Each Injection Visit
• Seroprotection Rate (SPR) = Percentage of Participants Who Have a Seroprotective Immune Response at Weeks 4, 8, 12, 18, 24, 28, 36, 44, and 52
• Percentage of Participants With Anti-HBsAg Greater Than or Equal to 100 mIU/mL at Weeks 4, 8, 12, 18, 24, 28, 36, 44, and 52
• Serum Anti-HBsAg Geometric Mean Concentration (GMC) at Weeks 4, 8, 12, 18, 24, 28, 36, 44, and 52
• SPR of Participants With Type 2 Diabetes Mellitus at Week 28

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either met the seroprotection threshold at week 28 or did not. The registry gives the number meeting the threshold and the analysis denominator in each group. The sponsor reports the difference between the two seroprotection rates in percentage points. The recalculation reports a risk difference, which is the difference between group proportions, using Engerix-B minus HEPLISAV-B. The direction of subtraction matters: reversing the order reverses the sign, without changing the underlying contrast.

What does a risk difference describe?

As a general statistical explanation, a risk difference compares the proportion with an outcome in one group against the proportion in another group. A value of zero represents equal observed proportions. Positive and negative values indicate which group has the greater proportion, according to the stated subtraction order. For this primary result, the recalculation uses Engerix-B relative to HEPLISAV-B, while the sponsor reports HEPLISAV-B relative to Engerix-B. Reading the group order alongside the sign prevents a direction-of-effect misunderstanding.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the data and the calculation method at the stated confidence level. It conveys uncertainty around the estimated contrast rather than providing a guarantee that the true value lies inside the interval. A narrower interval indicates greater precision than a wider interval on the same scale. The interval’s position relative to zero is relevant when considering whether the data are compatible with no difference under the calculation, but it does not by itself address clinical importance or study design assumptions.

How should the p-value be read?

The recalculated p-value is unadjusted. As a general explanation, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were true. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The registry does not post a p-value for the sponsor’s primary analyses, so the reported sponsor estimate and interval should not be treated as if they included one.

What is known about the analysis method?

The registry reports the primary endpoint counts, sponsor estimates, confidence intervals, and analysis-population definition. It does not report the specific statistical method used for the sponsor’s confidence interval or the details needed to reproduce that analysis. The recalculation is a simple unadjusted comparison from the posted summary statistics. It is not a substitute for an adjusted or prespecified sponsor analysis. Because the record does not flag a discrepancy, the posted sponsor analysis remains the primary reported result, while the recalculation offers a transparent comparison based on the counts.

Why distinguish the analysis population?

The modified intent-to-treat population includes randomized participants who received at least one study injection and had at least one post-injection immunogenicity evaluation. This definition differs from a population consisting of all randomized participants, because it requires both exposure to an injection and an evaluable post-injection assessment. The registry’s reported group denominators are the numbers used for this endpoint analysis. The record does not provide enough information to establish how participants without an endpoint assessment were handled, whether any values were imputed, or how additional protocol deviations were treated.

Why are binary outcomes sometimes over-dispersed?

As a general statistical explanation, over-dispersion occurs when observed variation is greater than a model assumes. It matters when a model’s uncertainty estimates rely on assumptions about how outcomes vary. The primary endpoint is binary, but the registry does not report a model-based analysis or an over-dispersion assessment. It would therefore be inappropriate to claim that over-dispersion was present, or that a particular correction was used. The posted summary supports interpretation of the group proportions and their stated uncertainty, not inference about unreported model diagnostics.

Overall, the statistical record supports describing a difference in observed week 28 seroprotection rates and the uncertainty reported around that difference. It does not provide the full protocol-level context for the sponsor’s non-inferiority and superiority tests. The original sample-size rationale, test sequence, missing-data procedures, and multiplicity strategy are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor reports a 95% confidence interval from 1.7 to 14.3 percentage points for the HEPLISAV-B minus Engerix-B seroprotection-rate difference. This interval describes the uncertainty around the reported difference on that scale. Its endpoints are both above zero, so the interval does not include no difference. The sponsor’s estimate is 8 percentage points.

The unadjusted recalculation reports the contrast with Engerix-B minus HEPLISAV-B. Its 95% confidence interval runs from -0.143 to -0.018. The interval is on the risk-difference scale and has the opposite sign convention to the sponsor’s percentage-point difference. Its endpoints also lie on the side indicating a lower observed rate in Engerix-B under the recalculation’s subtraction order. The registry record does not flag a discrepancy between the posted and recalculated results.

As a general explanation, interval width reflects precision: wider intervals allow a broader range of plausible effect sizes, while narrower intervals are more precise, given the method and data. An interval should not be interpreted as the range containing all individual outcomes, nor as a measure of the probability that one treatment is better. It also does not account for questions that are not represented in the calculation, such as unreported missing-data assumptions or multiplicity adjustments.

The sponsor’s interval and the recalculated interval are based on the primary analysis data as reported in different orientations. Their interpretation depends on the effect scale and group order. Precision around the immune-response difference does not establish precision about infection prevention or longer-term clinical outcomes, which are not represented by this endpoint.

12. Planning a Similar Trial: Sample Size

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

The planning illustration reports participants per arm for 80% power and participants per arm for 90% power. These are not total event counts. The calculation assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as its starting point and also considers planning for 75% and 50% of that observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 294 participants per arm for 80% power and 393 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 491 participants per arm for 80% power and 657 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 1,033 participants per arm for 80% power and 1,383 participants per arm for 90% power.

In plain terms, the 80% column describes the planned number per arm for a future study to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% column describes the corresponding number per arm for a 90% chance. The illustration is not observed power. Smaller effects require more participants to detect under these assumptions, which is why the planning figures increase as the assumed fraction of the observed effect gets smaller. These figures are planning illustrations, not evidence about the original study’s design choices.

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 = 0.899; treatment proportion p₁ = 0.818; average p̄ = 0.858.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4930 = 0.9663.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4897 = 0.4122.
4. n = (0.9663 + 0.4122)² / (-0.0805)² = 293.2, rounded up to 294 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 <- 0.898678414096916                          # control proportion
p1 <- 0.818181818181818                          # 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(985426)
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 = 294 (80% power), 393 (90% power)
 75% of observed effect: n per arm = 491 (80% power), 657 (90% power)
 50% of observed effect: n per arm = 1,033 (80% power), 1,383 (90% power)
power.prop.test: 293.2 
Simulated power at n = 294 per arm: 0.805 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis reports an 8 percentage-point difference in seroprotection rates for HEPLISAV-B relative to Engerix-B, with a 95% confidence interval from 1.7 to 14.3 percentage points. The registry lists that same estimate and interval under both non-inferiority and superiority analysis labels. It does not report a p-value for either sponsor analysis or the method used to calculate the interval.

The simple recalculation uses the posted group counts and reports Engerix-B minus HEPLISAV-B, so its estimate and interval carry the opposite sign. Its unadjusted p-value is 0.013. The two analyses point in the same direction when their subtraction order is taken into account. The registry record does not flag a discrepancy, so the sponsor’s own analysis is the principal reported analysis; the recalculation is an unadjusted check based on summary statistics, not a replacement for the sponsor’s analysis.

The record does not report the non-inferiority margin, prespecified testing sequence, or multiplicity procedure. The shared estimate and interval alone do not explain how the two analysis labels were evaluated. Those details are necessary for a fuller assessment of the sponsor’s inferential framework.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes, assessment weeks, and analysis labels, including primary and secondary immunogenicity analyses. It does not report whether the study used a formal strategy to control multiplicity, such as a prespecified testing hierarchy or an adjustment across hypotheses. It also does not report whether the non-inferiority and superiority analyses were linked through a specified sequence. Without that information, the interpretation of nominal or unadjusted statistical evidence across the full set of analyses is limited.

The primary outcome’s modified intent-to-treat population is defined as randomized participants who received at least one study injection and had at least one post-injection immunogenicity evaluation. The record gives the analysis denominators but does not report the number or characteristics of participants excluded from this population, or the reasons for missing endpoint assessments. The handling of missing week 28 results, including any imputation or sensitivity analyses, is not reported in the registry record.

The registry does not report a per-protocol population analysis or how protocol deviations were handled. It also does not specify whether the primary analysis was adjusted for baseline characteristics, how the confidence interval method was selected, or whether any prespecified subgroup analyses were planned. These details matter because different analysis populations and missing-data assumptions can affect an estimated treatment contrast.

The unadjusted recalculation uses the posted summary counts and does not address these unreported design and analysis choices. It is useful for checking the direction and approximate scale of the primary contrast, but it cannot recover participant-level information or determine whether the sponsor’s full analysis plan was followed. The record’s missing details are limits on interpretation, not evidence that a particular procedure was or was not used.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: renal failure chronic (4.6%), cardiac failure congestive (3.1%), renal failure acute (2.7%), pneumonia (2.0%), coronary artery disease (1.9%).

The registry reports serious adverse event counts for separate safety groups. In the HEPLISAV-B group, 68 participants were affected among 254 at risk; in the Engerix-B group, 76 were affected among 262 at risk. The record also reports other adverse event counts of 140 among 254 at risk for HEPLISAV-B and 146 among 262 at risk for Engerix-B. Death counts are 7 and 3, respectively. These figures are descriptive counts, not a comparative safety analysis with an estimated effect and confidence interval.

The registry lists renal failure chronic at 4.6%, cardiac failure congestive at 3.1%, renal failure acute at 2.7%, pneumonia at 2.0%, coronary artery disease at 1.9%, and anaemia at 1.6% among the most frequent serious terms reported. These terms provide context for the events recorded in a chronic kidney disease population; the registry summaries do not establish that an event was caused by a study injection.

The safety-group denominators differ from the primary immunogenicity analysis denominators, and the registry record does not explain all reasons for that difference. Counts alone do not account for follow-up time, event severity beyond the reported categorization, or other factors relevant to comparing safety. No medical conclusion should be drawn from these summaries alone.

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

The posted primary result describes a higher observed week 28 seroprotection rate in the HEPLISAV-B group than in the Engerix-B group. The sponsor reports the difference as 8 percentage points, with a 95% confidence interval from 1.7 to 14.3 percentage points. The recalculation reports the same directional contrast with the subtraction order reversed and gives an unadjusted p-value of 0.013. The registry record does not flag a discrepancy between the sponsor result and the recalculation.

The result is about the proportion meeting an antibody threshold, not the magnitude of antibody concentrations for every participant. It is also not a direct estimate of infection prevention, duration of protection, or a clinical outcome. The registry record does not report such outcomes as the primary endpoint. The findings therefore should not be extended beyond the immunogenicity question that was measured.

The result applies to the modified intent-to-treat analysis population defined in the registry, rather than automatically to all randomized participants or to every adult with chronic kidney disease. The subgroup and secondary outcomes may add context, but they do not erase uncertainties about multiplicity, missing data, or the sponsor’s testing procedures. The non-inferiority margin and analysis sequence are not reported, so the labels attached to the sponsor analyses cannot be fully assessed from the registry alone.

As a general statistical point, an estimate and confidence interval describe evidence under the assumptions of the analysis; they do not establish the practical importance of the effect. Decisions about clinical value require context beyond the posted statistics. The data support a comparison of measured seroprotection at week 28, with the stated uncertainty, and no broader conclusion should be inferred from that endpoint alone.

18. Why This Trial Matters Statistically

This trial illustrates how an immunogenicity endpoint can be translated into a binary comparison: whether each participant meets a defined antibody threshold at a specified assessment time. The registry provides both the group counts and the sponsor’s estimate, allowing the direction and scale of the primary contrast to be interpreted alongside its confidence interval. The modified intent-to-treat definition also makes explicit that the primary analysis is based on randomized participants with injection exposure and a post-injection immunogenicity evaluation.

The record is useful for statistical reading because it presents the primary result under non-inferiority and superiority labels while leaving some of the testing framework unreported. The estimate and interval are identical in those posted analyses, but the margin, testing sequence, and multiplicity strategy are not reported. This highlights why a result’s label cannot replace information about the prespecified hypothesis and method.

The secondary outcomes and safety summaries show why endpoint-specific interpretation matters. A threshold-based immune response, antibody concentration, subgroup result, adverse event count, and clinical outcome answer different questions. The registry’s numerical summaries allow readers to distinguish those kinds of evidence rather than treating them as interchangeable.

Finally, the planning illustration demonstrates the relationship between an assumed effect size and the number of participants needed under stated assumptions. It is distinct from the trial’s original design and from observed power. Together, these features make the record a case study in reading effect direction, analysis populations, uncertainty, and missing statistical-plan detail without overextending what the endpoint can establish.

19. Limitations

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

The registry record does not report the statistical method used for the sponsor’s confidence interval, the non-inferiority margin, or the sequence linking the non-inferiority and superiority analyses. It also does not report a p-value for the sponsor’s analyses. These omissions constrain independent evaluation of the sponsor’s inferential framework.

The primary analysis population requires receipt of at least one study injection and at least one post-injection immunogenicity evaluation. The record does not report how many participants lacked a week 28 assessment, why values were missing, or how missing endpoint data were handled. It does not describe imputation or sensitivity analyses. Consequently, the potential effect of missing outcomes cannot be assessed from the posted summaries.

The endpoint measures whether an antibody threshold was reached, rather than infection or another clinical outcome. The registry also lists repeated assessment times and secondary outcomes but does not report a multiplicity strategy. Subgroup and secondary findings therefore need cautious interpretation, particularly where the analysis plan is unavailable.

The safety summaries give counts and selected serious-event terms but do not provide comparative effect estimates or confidence intervals. The safety and immunogenicity groups have different denominators, and the record does not explain the reasons. The record also does not report enough detail to assess differences in follow-up or event ascertainment. These limitations do not negate the posted result, but they restrict what can be concluded from registry summaries alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparing Safety and Immunogenicity of HEPLISAV-B® to Engerix-B® in Chronic Kidney Disease (CKD) Patients — NCT00985426.
• Registry record last updated 2021-05-19; status last verified 2021-04.
• Results first posted 2020-12-16.
• 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

NCT00985426 is a completed phase 3 randomized, double-masked, parallel-group study comparing HEPLISAV-B with Engerix-B in adults aged 18 to 75 years with chronic kidney disease. Reported enrollment was 521. The primary endpoint was week 28 seroprotection, defined by an anti-HBsAg level greater than or equal to 10 mIU/mL, in a modified intent-to-treat population.

The sponsor reports an 8 percentage-point difference for HEPLISAV-B relative to Engerix-B, with a 95% confidence interval from 1.7 to 14.3 percentage points. The unadjusted recalculation uses the reverse comparison order and reports p = 0.013. The registry record does not flag a discrepancy. Details of the original sample-size assumptions, missing-data handling, multiplicity strategy, and sponsor analysis methods are not reported in the registry record.