A Study to Compare Tenofovir DF Versus the Combination of Emtricitabine Plus Tenofovir DF for the Treatment of Chronic Hepatitis B in Patients With Normal Alanine Aminotransferase (ALT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare Tenofovir DF Versus the Combination of Emtricitabine Plus Tenofovir DF for the Treatment of Chronic Hepatitis B in Patients With Normal Alanine Aminotransferase (ALT) (NCT00507507), a randomized phase 2 study. The primary outcome is Percentage of Participants With HBV DNA < 400 Copies/mL at Week 192.

2. Clinical Question

The clinical question concerns antiviral activity over an extended treatment period. The primary endpoint operationalizes viral suppression using a specified HBV DNA threshold at Week 192. Other stated efficacy areas included serological response, biochemical response, and development of drug-resistant mutations; safety and tolerability were also evaluated through adverse-event and laboratory monitoring.

The study was randomized, double-blind, and parallel-group. Its central comparison is therefore the difference in endpoint results between participants assigned to the two regimens, rather than a comparison with no treatment. The registry record describes the target population and treatment strategies, but does not report additional eligibility details or enough information to establish how broadly the results apply beyond the study participants.

3. Trial Design

This was a randomized, double-blind, parallel-group Phase 2 study with quadruple masking recorded in the registry. Enrollment was 126. Participants were assigned in a 1:1 ratio to tenofovir DF monotherapy or FTC plus tenofovir DF. The monotherapy group received tenofovir DF with placebo to match FTC; the combination group received both FTC and tenofovir DF. Both regimens were once daily.

The stated objective was to compare antiviral activity in people with chronic hepatitis B in the immune tolerant phase. The efficacy areas included reduction in HBV DNA, serological response, changes in liver enzymes, and drug-resistant mutations. Safety and tolerability were evaluated through routine monitoring for adverse events and laboratory changes. The registry record lists a study start of 2007-09 and primary completion of 2012-02, and the study status is completed.

Participants were intended to continue blinded study medication until the last participant reached Week 192. Participants who permanently discontinued study drug on or before Week 192 were to be followed without treatment for 24 weeks, or until alternative HBV therapy began, whichever came first. A specific follow-up arrangement was described for participants discontinuing on or after Week 48 because of HBsAg loss or seroconversion to anti-HBs.

The primary endpoint was assessed at Week 192. Its analysis population included randomized participants who received at least one dose. The registry record does not report the original sample-size justification, the detailed sequence-generation or allocation-concealment procedures, or a full statistical analysis plan. It also does not report interim-analysis procedures. These details should not be inferred from the randomized and masked design labels.

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: 309 participants were screened and 129 were randomized; 126 randomized participants received at least one dose of study drug, and comprise the Safety Analysis Set and the Full Analysis Set.

Treatment Period

Reasons for not completing this period:

24-week Treatment-free Follow-up Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: participants who were randomized and received at least one dose of study drug

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: Participants who were randomized and treated were analyzed for baseline characteristics.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With HBV DNA < 400 Copies/mL at Week 192, measured over Week 192.

The primary endpoint was the percentage of participants with HBV DNA below 400 copies/mL at Week 192. It expresses the proportion in each treatment group meeting a defined viral-load threshold at a specified study time. HBV DNA is a measure of the amount of hepatitis B virus material detected in blood; defining a threshold turns the measurement into a binary outcome for this analysis: a participant either met the criterion or did not.

A threshold-based endpoint is useful because it gives a clinically interpretable description of how many participants reached a stated level of viral suppression. It also makes the treatment groups directly comparable as proportions. It does not, by itself, describe the full distribution of HBV DNA values or the degree of viral-load reduction among participants who did not reach the threshold. The secondary outcomes include changes in HBV DNA from baseline, which address a different aspect of response.

The primary analysis treated missing Week 192 data as failure to meet the endpoint. This rule makes the handling of missing observations explicit, but it also means the reported percentages reflect both observed endpoint status and the specified classification of missing participants. The endpoint is not a direct measure of symptoms, long-term clinical events, or safety. Its interpretation should remain tied to the viral suppression criterion and time point that were defined in the registry record.

7. Results Posted in the Registry

• FTC+Tenofovir DF: 75.8% (47/62) versus 54.7% (35/64) on control; risk difference 21.1 percentage points (95% CI 4.9 to 37.3), risk ratio 1.39 (1.06–1.80); 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.

Change From Baseline in HBV DNA at Week 48

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • FTC+Tenofovir DF: mean -6.49 versus -6.22 on control; difference -0.27 (95% CI -0.48 to -0.06), standardized effect d = -0.45; z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FTC+Tenofovir DF than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in HBV DNA at Week 96

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • FTC+Tenofovir DF: mean -6.55 versus -6.46 on control; difference -0.09 (95% CI -0.45 to 0.27), standardized effect d = -0.09; z-test p = 0.628.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FTC+Tenofovir DF and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HBV DNA at Week 144

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • FTC+Tenofovir DF: mean -6.62 versus -6.66 on control; difference 0.04 (95% CI -0.35 to 0.43), standardized effect d = 0.04; z-test p = 0.839.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FTC+Tenofovir DF and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the view beyond the Week 192 threshold used for the primary endpoint. They include HBV DNA suppression at other thresholds and times, changes from baseline in HBV DNA, ALT normalization, and HBeAg loss. The posted continuous results show that the direction and apparent size of group contrasts are not uniform across assessment times, and the uncertainty around those contrasts also varies. This means the secondary outcomes should be viewed as complementary measures rather than as a single consistent estimate of one underlying effect.

These measures relate to the primary result because they assess other aspects or time points of viral and biochemical response. They do not redefine the primary endpoint or establish its result independently. A change in mean HBV DNA and the percentage crossing a threshold are different summaries: one describes average change, while the other counts participants meeting a defined cutoff. They can therefore tell different parts of the response story without being contradictory.

The registry lists multiple outcomes and analyses. When many comparisons are examined, the chance of seeing a small p-value by chance somewhere among them can increase. Unadjusted secondary p-values do not account for that broader set of tests, and the record does not report a multiplicity adjustment. For that reason, secondary signals generally carry less confirmatory weight than a primary outcome identified for the main comparison.

The secondary results can help generate questions and indicate where patterns may merit further evaluation, but they should not be treated as independent confirmations merely because a result appears notable. Interpretation should consider the endpoint definition, time point, analysis population, missing observations, estimate size, and interval where available. The registry record does not report all planned-versus-reported outcome details or a complete multiplicity strategy, so the degree of selection among secondary analyses cannot be assessed from the record alone.

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

• Percentage of Participants With HBV DNA < 400 Copies/mL at Weeks 48, 96, and 144
• Percentage of Participants With HBV DNA < 169 Copies/mL at Weeks 48, 96, 144, and 192
• Change From Baseline in HBV DNA at Week 48
• Change From Baseline in HBV DNA at Week 96
• Change From Baseline in HBV DNA at Week 144
• Change From Baseline in HBV DNA at Week 192
• Number of Participants With Normal Alanine Aminotransferase (ALT) at Weeks 48, 96, 144, and 192
• Number of Participants With Hepatitis B e Antigen (HBeAg) Loss at Weeks 48, 96, 144, and 192

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: meeting or not meeting the HBV DNA threshold at Week 192. A percentage is the proportion meeting that criterion within a treatment group. The primary comparison can be expressed as a risk difference: the proportion in the combination group minus the proportion in the monotherapy group. A risk difference is an absolute contrast on the proportion scale. It does not describe a relative increase, and it should not be confused with an odds ratio or risk ratio.

The recalculated risk difference is 0.211, and its 95% confidence interval runs from 0.049 to 0.373. The interval quantifies sampling uncertainty around the unadjusted difference under the calculation's assumptions. An interval spanning values near zero would include little or no difference among the compatible values; the reported interval instead has both endpoints above zero. This statistical feature does not remove uncertainty about generalizability, missing outcomes, bias, or whether the endpoint captures outcomes important beyond the measured viral threshold.

The registry reports a Fisher Exact test for the primary comparison, with p = 0.016. Fisher Exact testing evaluates how compatible the observed allocation of binary outcomes is with a null hypothesis of no association between treatment group and endpoint, under the test's assumptions. The recalculated unadjusted p-value is 0.013. A p-value is not the probability that the null hypothesis is true, nor does it measure the size of a treatment difference. It indicates how unusual data at least as incompatible with the null as the observed data would be if the null model applied.

For continuous secondary outcomes, such as change from baseline in HBV DNA, the registry reports group means and standard deviations. A mean summarizes the arithmetic center of observed values, while the standard deviation describes their spread. The recalculated mean difference is the combination-group mean minus the monotherapy-group mean. Its confidence interval reflects uncertainty in that unadjusted mean contrast. The posted sponsor analyses for these secondary outcomes use Wilcoxon (Mann-Whitney) tests, which compare the distributions or ranks of observations rather than directly testing a difference in means. Accordingly, a p-value from that test need not correspond exactly to a mean-difference confidence interval calculated from summary statistics.

General statistical point: the mean and standard deviation are most informative when the distribution and the estimand make them appropriate summaries. A rank-based test can be useful when a comparison is framed without relying on a normal-distribution model for individual observations. It does not automatically test the difference in means, and a significant rank-based result should not be translated into a specific mean difference without additional assumptions.

General statistical point: over-dispersion means that variability is greater than a model expects. When present, treating observations as less variable than they are can make standard errors too small and intervals too narrow. The registry record does not report an over-dispersion model for the primary binary outcome, and the summary results alone do not establish whether over-dispersion was assessed. No such model should be assumed.

What does randomization contribute?

Random assignment aims to make treatment groups comparable with respect to measured and unmeasured characteristics, on average, before treatment. It supports a causal interpretation of a between-group contrast when implementation, follow-up, outcome measurement, and analysis preserve the benefits of randomization. The registry identifies the trial as randomized and gives the allocation ratio, but does not report all procedural details needed to assess allocation concealment or departures from assignment.

What does masking contribute?

Masking is intended to reduce the chance that knowledge of assigned treatment influences participant experience, clinical management, outcome assessment, or reporting. The record identifies quadruple masking and describes matching placebo in the monotherapy group. It does not identify the specific roles covered by the masking label, so those roles should not be guessed.

How should missing outcomes be understood?

The primary endpoint description states that participants with missing data were counted as not achieving the criterion. This is a failure classification, not an estimate of what their unobserved Week 192 values would have been. Its interpretation relies on the analysis rule and can be affected by how many outcomes are missing and why. The record does not report a detailed sensitivity analysis for alternative missing-data assumptions.

What does a p-value add?

A p-value summarizes compatibility with a specified null model; it does not convey the magnitude, precision, clinical importance, or durability of an effect by itself. The risk difference and its confidence interval provide magnitude and uncertainty on an absolute scale, while the p-value gives a test-based summary. All are unadjusted summaries in the displayed recalculation. The registry record does not report whether the primary test was part of a broader multiplicity procedure.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.211, with a 95% confidence interval from 0.049 to 0.373. The interval gives a range of effect sizes reasonably compatible with the observed data under the calculation's assumptions. Its endpoints are not predictions for individual participants, and the interval does not account automatically for every potential source of uncertainty, such as missing-data assumptions, study conduct, or differences between this study population and other populations.

The interval is on an absolute proportion-difference scale, which makes it interpretable as a contrast between the proportions meeting the endpoint in the two randomized groups. The interval's lower and upper limits are both positive, but the width indicates that the estimated difference is not known with exact precision. The point estimate should therefore be read together with the interval rather than as a single definitive value.

The group percentages are based on 64 participants assigned to tenofovir DF and 62 assigned to FTC plus tenofovir DF. Estimates from finite groups have sampling uncertainty even when randomization is used. The confidence interval represents one component of that uncertainty. It does not resolve whether all missing outcomes would have followed the same pattern as observed outcomes, and the primary rule counted missing participants as not meeting the criterion.

The registry's Fisher Exact p-value and the recalculated confidence interval answer related but distinct questions and arise from different summaries or methods. The interval helps assess the range of plausible absolute contrasts; the p-value summarizes compatibility with a null hypothesis under a test. Neither should be interpreted as a guarantee that the true effect lies within the interval or that the observed estimate will recur in another study.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants, for these binary and continuous outcomes. They are planning illustrations based on the observed effect, not the original trial's design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial's original sample-size assumptions and justification are not reported in the registry record.

The 80% power column indicates the illustrative number of participants per arm that would be needed to 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 target for a 90% chance. These are design calculations, not a measure of what the completed trial's power was after results were observed.

Rows for planning at 100% of the observed effect use the full observed estimate as the target; rows for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so the illustrative participant requirements rise as the target effect becomes smaller. This pattern is a general feature of power planning, not evidence that the smaller effect fractions are known or likely true.

The resulting figures are sensitive to the assumptions and to the observed effect used as a starting point. In particular, an effect estimated in a study can be imprecise, and a planning exercise that treats it as the target does not establish a reliable future effect. The sample-size curve should be read as a visual rendering of the same planning relationship, not as a forecast of results or a substitute for a design calculation based on a prospectively chosen effect.

These values are not observed power. Observed power calculated from an effect estimate after a trial is complete does not provide an independent account of the evidence; the observed estimate and its uncertainty are more informative for interpreting the result.

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 = 0.547; treatment proportion p₁ = 0.758; average p̄ = 0.652.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6734 = 1.3199.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6567 = 0.5527.
4. n = (1.3199 + 0.5527)² / (0.2112)² = 78.6, rounded up to 79 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 <- 0.546875                          # control proportion
p1 <- 0.758064516129032                          # 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(507507)
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 = 79 (80% power), 105 (90% power)
 75% of observed effect: n per arm = 146 (80% power), 195 (90% power)
 50% of observed effect: n per arm = 337 (80% power), 451 (90% power)
power.prop.test: 78.6 
Simulated power at n = 79 per arm: 0.816 (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 registry reports the sponsor's primary comparison using a Fisher Exact test, with p = 0.016. The simple unadjusted recalculation from the posted group counts gives a risk difference of 0.211, a 95% confidence interval from 0.049 to 0.373, and p = 0.013. The trial record does not mark a discrepancy.

These figures are not identical because they summarize the comparison in different ways. Fisher Exact is the reported test for the binary outcome. The recalculated summaries provide an absolute difference and interval from the posted group results, with an unadjusted test-based p-value. Small differences between p-values can arise from differing statistical procedures; p-values are not unique properties of the percentages alone.

The recalculation is not a replacement for the sponsor's analysis plan or a reconstruction of participant-level analysis. It is an unadjusted calculation from the summary counts. The sponsor-reported result should be interpreted as the registry's analysis, while the recalculated risk difference and interval offer a complementary view of magnitude and precision. The registry record does not report enough detail to establish whether any additional covariate adjustment or other analysis informed the sponsor's primary conclusion.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and numerous secondary outcomes, with multiple analyses reported. Testing several outcomes or time points creates a multiplicity issue: even if no true differences exist, repeated testing can produce apparently notable results by chance. A pre-specified hierarchy or adjustment procedure can help control that issue. The record does not report whether such a hierarchy or adjustment was used for the secondary analyses, so their p-values should be treated as unadjusted unless the registry states otherwise.

The primary endpoint description specifies that participants with missing data were considered not to have achieved the criterion. This makes the classification rule transparent, but the record does not provide a full account of missingness by reason, sensitivity analyses under alternative assumptions, or details of how all post-discontinuation observations were handled in the primary analysis. The stated treatment-free follow-up plan does not by itself establish how missing Week 192 outcome measurements were addressed beyond the stated failure classification.

The primary population was the Full Analysis Set, defined as randomized participants who received at least one dose of study drug. This is not identical to an analysis of every randomized participant if any randomized participant did not receive treatment. The record does not report the counts or outcomes for any such participants, or describe a separate per-protocol analysis in the primary result.

These limitations do not invalidate the posted comparison, but they shape its interpretation. Missing-data rules can affect the estimated percentages, while multiplicity affects how confidently secondary findings can be treated as confirmatory. The registry record does not report the original statistical analysis plan, interim analyses, or the complete set of decisions made before outcome data were examined. Those details cannot be inferred from the results listing.

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: urinary tract infection (1.6%), abortion spontaneous (1.6%), ovarian cyst (1.6%), appendicitis (1.6%), gastroenteritis (1.6%).

During the treatment period, the registry lists serious adverse events for 6 of 64 participants in the tenofovir DF group and 3 of 62 participants in the FTC plus tenofovir DF group. During the 24-week treatment-free follow-up period, the listed serious adverse events were 0 of 26 and 0 of 29, respectively. The follow-up groups are not the full original randomized groups; these are the numbers recorded as at risk for that period.

The registry also lists other adverse events for 41 of 64 participants and 39 of 62 participants during treatment, and 2 of 26 and 7 of 29 during treatment-free follow-up, in the same group order. These counts describe reported participants, not necessarily the number of individual events. The serious-event terms listed include urinary tract infection, spontaneous abortion, ovarian cyst, appendicitis, gastroenteritis, and hepatitis B, each reported as 1.6%.

The record does not report death counts in the listed safety summary; absence of a reported count should not be interpreted as evidence that no deaths occurred. These descriptive counts do not by themselves establish a causal difference in safety between groups. They should be read alongside the treatment and follow-up periods, the changing numbers at risk, and the limits of the registry safety summary.

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

The primary result describes the proportion of participants meeting a defined HBV DNA threshold at Week 192 in two randomized treatment groups. The posted percentages and unadjusted comparison indicate a difference between the groups on that endpoint in this study. The confidence interval provides a range of compatible absolute differences, while the sponsor-reported Fisher Exact test supplies a separate test-based summary.

This result does not establish that every participant in either group experienced the same response, nor does it describe the full distribution of viral-load values. It does not establish effects on symptoms, liver outcomes, transmission, or other outcomes that are not reported as the primary endpoint. The trial assessed other efficacy and safety outcomes, but their presence does not make them interchangeable with the Week 192 viral suppression measure.

The findings are specific to the participants enrolled, the regimens compared, the endpoint definition, the analysis population, and the missing-data rule. The title describes patients with normal ALT, and the study objective identifies participants in the immune tolerant phase of HBV infection. The registry record does not provide enough detail to determine how the result applies to populations with different characteristics or treatment histories.

Statistical evidence is not medical advice. A p-value does not establish clinical importance, and a confidence interval does not eliminate uncertainty. Safety counts are descriptive and do not establish a causal safety comparison. Decisions about treatment require consideration beyond these posted statistics and are outside the scope of this statistical interpretation.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result is best read through both its endpoint and its comparison. A percentage meeting a viral-load threshold is readily interpretable, but it compresses a continuous biological measurement into a yes-or-no classification. The separate HBV DNA change outcomes capture another dimension of response, making clear that no single summary fully represents all aspects of antiviral activity.

It also shows the value of separating effect size from statistical testing. The absolute risk difference and its interval communicate the estimated contrast and its precision, while the Fisher Exact p-value addresses compatibility with a null hypothesis under a particular test. Neither is a substitute for the other, and neither resolves questions about clinical relevance, generalizability, missing data, or safety.

The trial's long-term endpoint and treatment-free follow-up plan also highlight that outcome timing and follow-up context matter. The primary measure is tied to Week 192; safety summaries distinguish the treatment period from the 24-week treatment-free follow-up. Those windows answer different descriptive questions and should not be collapsed.

Finally, multiple secondary outcomes require disciplined interpretation. They can enrich understanding, but unadjusted tests across many measures have less confirmatory force than a primary comparison. This trial therefore offers a useful example of reading randomized evidence with attention to endpoint definition, analysis population, missing-data handling, uncertainty, and multiplicity rather than relying on a single p-value.

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.

The registry record does not report the original sample-size justification, so it is not possible to determine the assumptions used to select enrollment or whether the study was designed around a particular clinically meaningful difference. The planning illustrations based on observed effects are not a substitute for that information. A complete statistical analysis plan, including any planned analysis hierarchy, covariate adjustment, and interim analyses, is also not reported.

The primary endpoint counts missing Week 192 observations as failures. That is a clear rule, but the registry record does not provide a detailed account of the number and reasons for missing measurements or sensitivity analyses using alternative assumptions. The treatment and follow-up plans describe intended participant follow-up, but do not establish that all planned assessments were obtained.

The record identifies randomization and quadruple masking, but does not detail the randomization sequence, allocation concealment, or the roles covered by masking. Those procedural details matter when assessing potential selection or measurement bias. The primary analysis uses the Full Analysis Set of randomized participants who received at least one dose; the record does not provide enough detail to assess the influence of any randomized participants excluded by that definition.

Secondary outcomes involve multiple measures and time points, while a multiplicity procedure is not reported. Safety summaries are descriptive, include different numbers at risk across periods, and do not report deaths in the listed data. They cannot establish comparative safety on their own. These limitations are specific to the information available in the registry record and should not be filled in by assumptions about common trial practice.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare Tenofovir DF Versus the Combination of Emtricitabine Plus Tenofovir DF for the Treatment of Chronic Hepatitis B in Patients With Normal Alanine Aminotransferase (ALT) — NCT00507507.
• Registry record last updated 2015-07-17; status last verified 2015-07.
• Results first posted 2013-08-08.
• 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

NCT00507507 is a completed randomized, double-blind, parallel-group Phase 2 study sponsored by Gilead Sciences. It enrolled 126 participants with chronic hepatitis B and compared once-daily tenofovir DF with once-daily FTC plus tenofovir DF. The primary endpoint was the percentage with HBV DNA below 400 copies/mL at Week 192 in the Full Analysis Set, with missing outcomes treated as not meeting the criterion.

The registry reports 54.7% in the tenofovir DF group and 75.8% in the combination group. Its primary Fisher Exact test reports p = 0.016; the unadjusted recalculation gives a risk difference of 0.211 with a 95% confidence interval from 0.049 to 0.373 and p = 0.013. The record also lists secondary efficacy outcomes and descriptive safety counts. It does not report the original sample-size justification, full analysis plan, multiplicity approach, or detailed sensitivity analyses for missing data.