AVJ-301 Clinical Trial: A Clinical Evaluation of AVJ-301 (Absorb™ BVS) in Japanese Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for AVJ-301 Clinical Trial: A Clinical Evaluation of AVJ-301 (Absorb™ BVS) in Japanese Population (NCT01844284), a randomized na study. The primary outcome is Number of Participants With Target Lesion Failure (TLF).

2. Clinical Question

The study asked whether the Absorb™ bioresorbable vascular scaffold could be evaluated against an approved metallic drug-eluting stent in Japanese participants treated for ischemic heart disease caused by de novo native coronary artery lesions. The primary question concerned target lesion failure at 1 year, a composite of cardiac death, target vessel myocardial infarction, and ischemic-driven target lesion revascularization.

The randomized allocation was 2:1, with a planned enrollment of 400. The posted primary endpoint counts are 11 of 265 for Absorb BVS and 5 of 133 for XIENCE. These counts describe the participants analyzed for the endpoint, rather than the planned enrollment. They are the observed event counts used in the posted comparison; they do not by themselves establish that one device is better or worse, or resolve the trial's stated non-inferiority question.

3. Trial Design

This was a prospective, randomized, active-control, single-blind, multicenter clinical trial in a Japanese population. The registry describes a parallel-group design and random allocation in a 2:1 ratio. The planned enrollment was 400. The study is marked completed, with a start date of 2013-04 and primary completion in 2015-01.

The intervention was Absorb BVS, described in the trial title as an everolimus-eluting bioresorbable vascular scaffold. The active comparator was the metallic drug-eluting stent XIENCE PRIME®/XIENCE Xpedition™. The registry's brief summary characterizes the trial as a non-inferiority evaluation of safety and effectiveness. The phase is recorded as NA; a further phase description is not reported in the registry record.

Single-blind status is recorded, but the identity of the blinded group or groups is not reported in the registry record. The randomization method, concealment procedures, site count, and detailed eligibility criteria are also not reported in the registry record. The planned allocation ratio differs from the analyzed arm sizes posted for the primary endpoint, which are 265 for Absorb BVS and 133 for XIENCE. The registry explains that endpoint counts include participants with available follow-up data at the specified time frame.

The primary endpoint was assessed at 1 year. It was a participant count for a composite outcome, target lesion failure, comprising cardiac death, target vessel myocardial infarction, or ischemic-driven target lesion revascularization. The record also lists early secondary outcomes measured through 7 days after the index procedure, during the in-hospital period. No detailed schedule of follow-up visits or data-collection procedures is reported in the registry record.

The registry record does not report the trial's original sample-size justification, the non-inferiority margin, or the prespecified statistical analysis plan. Those omissions limit how fully the stated design objective can be connected to the posted endpoint counts and unadjusted comparison.

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: ITT population. The number of participants analyzed includes subjects who had available follow up data at that time frame.

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 Number of Participants With Target Lesion Failure (TLF), measured over 1 year.

Target lesion failure (TLF) is the primary endpoint, measured as the number of participants with an event at 1 year. The registry defines the composite as cardiac death, target vessel myocardial infarction (TV-MI), or ischemic-driven target lesion revascularization (ID-TLR). A composite endpoint combines clinically different events into one outcome: a participant is counted as having TLF if an event meeting one of the listed components occurs.

This kind of endpoint can provide a single summary of several ways a treated lesion or its related vessel may be associated with a serious event or a need for further treatment. It also requires careful interpretation. The total TLF count does not show how many participants experienced each component, whether one component accounts for most of the composite, or whether participants had more than one component. Component-specific primary results are not reported in the registry record.

The endpoint is a count of participants, not a time-to-event estimate or a measure of the number of events. The registry describes the analysis population as ITT, while noting that the number analyzed includes participants with available follow-up data at the specified time frame. Therefore, the posted counts and arm sizes should be read as the available-follow-up endpoint data reported for 1 year.

The endpoint's composite definition makes it relevant to the stated comparison, but the registry record does not report the component adjudication details, the non-inferiority margin, or the sponsor's formal inferential analysis. The observed TLF counts alone cannot establish non-inferiority.

7. Results Posted in the Registry

• XIENCE PRIME/XIENCE Xpedition: 3.8% (5/133) versus 4.2% (11/265) on control; risk difference -0.4 percentage points (95% CI -4.4 to 3.6), risk ratio 0.91 (0.32–2.55); unadjusted two-proportion z-test p = 0.851.

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.

Number of Participants With Any Death/Any MI/Revascularization (DMR)

• 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:
  • XIENCE PRIME/XIENCE Xpedition: 0.8% (1/133) versus 1.1% (3/265) on control; risk difference -0.4 percentage points (95% CI -2.3 to 1.6), risk ratio 0.66 (0.07–6.32); unadjusted two-proportion z-test p = 0.720.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE PRIME/XIENCE Xpedition and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Target Vessel Failure (TVF)

• 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:
  • XIENCE PRIME/XIENCE Xpedition: 0.8% (1/133) versus 1.1% (3/265) on control; risk difference -0.4 percentage points (95% CI -2.3 to 1.6), risk ratio 0.66 (0.07–6.32); unadjusted two-proportion z-test p = 0.720.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE PRIME/XIENCE Xpedition and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Target Lesion Failure (TLF)

• 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:
  • XIENCE PRIME/XIENCE Xpedition: 0.8% (1/133) versus 1.1% (3/265) on control; risk difference -0.4 percentage points (95% CI -2.3 to 1.6), risk ratio 0.66 (0.07–6.32); unadjusted two-proportion z-test p = 0.720.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE PRIME/XIENCE Xpedition and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists early secondary participant-count outcomes through 7 days after the index procedure, including any death, any myocardial infarction, or revascularization (DMR), target vessel failure (TVF), and target lesion failure (TLF). For each of the three posted early comparisons, the event counts are 3 of 265 in the Absorb BVS arm and 1 of 133 in the XIENCE arm. The posted risk difference is -0.004, the confidence interval runs from -0.023 to 0.016, and the unadjusted p-value is 0.72.

These early outcomes have a shorter timeframe than the primary TLF outcome at 1 year. They therefore address events during the in-hospital period after the index procedure rather than the full primary follow-up period. The early TLF measure shares the primary endpoint name, but its timeframe is different. DMR and TVF also differ in their component definitions from the 1-year primary composite. These endpoint distinctions matter when relating secondary observations to the primary result.

The posted early comparisons show few events in each arm and wide uncertainty around the risk difference. They do not provide a precise independent confirmation of the primary finding. The primary outcome remains the designated endpoint, while secondary outcomes can add context about other event definitions and time windows. The registry record does not list reported analyses for these secondary outcomes or provide a sponsor-reported interpretation.

General statistical explanation: when multiple secondary outcomes are examined, the chance of at least one apparently unusual result can increase unless the analysis accounts for multiplicity. No multiplicity adjustment or hierarchy for secondary outcomes is reported in the registry record. Accordingly, secondary results should carry less inferential weight than a prespecified primary result and should generally be regarded as exploratory. The record lists 101 posted secondary outcomes and 102 outcome measures, but does not provide a multiplicity plan that explains how results across outcomes were to be interpreted.

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

• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)
• Number of Participants With Any Death/Any MI/Revascularization (DMR)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is an unadjusted comparison of the proportion of participants with target lesion failure in each arm. Its effect measure is the risk difference: the event proportion in the Absorb BVS arm minus the event proportion in the XIENCE arm. General statistical interpretation: a risk difference of zero corresponds to equal observed proportions, a negative estimate indicates a lower observed proportion in the first arm, and a positive estimate indicates a higher observed proportion in the first arm. The posted risk difference is -0.004.

What does an unadjusted comparison mean?

An unadjusted comparison uses the observed outcome counts and analyzed group sizes without accounting for other participant characteristics or prognostic factors. It provides a direct summary of the difference in observed proportions. Randomization is intended to support a fair comparison of treatment groups, but an unadjusted calculation does not itself address missing follow-up, departures from the assigned treatment, or other analysis decisions. The registry record does not report a covariate-adjusted primary analysis or a sponsor-reported inferential analysis.

The posted data give 11 TLF participants among 265 analyzed in the Absorb BVS arm and 5 among 133 analyzed in the XIENCE arm. The risk difference estimate and confidence interval are recalculated from the posted summary statistics. The registry record does not report a discrepancy between those recalculations and a sponsor analysis; it also does not list a sponsor-reported analysis for this outcome. The posted recalculation should therefore be understood as a simple unadjusted summary, not as the trial's full prespecified analysis.

How should the p-value be read?

The unadjusted p-value is 0.851. General statistical explanation: a p-value describes how compatible the observed data are with a specified null model, assuming that model and the calculation's assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A large p-value does not establish that two treatments are equivalent. In a non-inferiority study, the key inferential question is whether the confidence interval excludes effects beyond the prespecified non-inferiority margin, under the trial's planned analysis. The margin and that formal analysis are not reported in the registry record.

What does the confidence interval add?

The 95% confidence interval for the risk difference extends from -0.044 to 0.036. General statistical explanation: a confidence interval expresses the range of values reasonably compatible with the observed data under the method used. Its width reflects statistical precision; a wider interval leaves more uncertainty about the underlying difference. Because this interval includes zero and values on both sides of zero, the observed estimate does not precisely distinguish the direction of the difference. It also cannot be interpreted against a non-inferiority threshold that is not reported.

The confidence interval's meaning depends on the calculation and analysis population. The posted comparison is unadjusted and uses participants with available follow-up as described by the registry. The record does not report a detailed missing-data method, an alternative analysis population, or sensitivity analyses. These omissions prevent assessment of whether different handling of missing outcomes or different analysis choices would materially change the estimate.

Why is the stated non-inferiority design not enough?

A non-inferiority design is intended to assess whether an intervention is not unacceptably worse than a comparator, according to a prespecified margin. General explanation: that margin defines how much difference can be accepted for the purpose of the trial, and the statistical test and confidence interval must be interpreted relative to it. Merely describing a trial as non-inferiority does not reveal the margin, the planned analysis set, or the conclusion. The registry record does not report the margin, the sample-size rationale, or the sponsor's analysis results. As a result, the unadjusted risk difference cannot independently answer the non-inferiority question.

Randomization is listed as 2:1 and the study as single-blind and parallel-group. These design features provide context, but the registry record does not specify the random-sequence generation, allocation concealment, or who was blinded. The record identifies an ITT population for the primary outcome and clarifies that endpoint participants analyzed had available follow-up. No details are reported on adherence, crossover, or protocol deviations, so their handling cannot be assessed.

How do secondary outcomes fit the analysis?

The secondary outcomes are participant counts, including early DMR, TVF, and TLF outcomes through 7 days after the index procedure. The registry record lists no reported analyses for these outcomes. The posted comparisons are unadjusted summaries, and no adjustment plan across secondary endpoints is reported. General statistical explanation: when many outcomes are examined, some may appear noteworthy by chance even if there is no underlying effect. Without a prespecified multiplicity strategy, secondary findings are best treated as exploratory rather than as independent confirmation of the primary result.

The registry identifies the primary outcome and its timeframe, but it does not report a full statistical analysis plan. The precise tests, interval construction details, handling of repeated events or competing events, subgroup analyses, and interim analyses are not reported in the registry record. No assumptions about those choices should be inferred from the recalculated summary comparison.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.004, with a 95% confidence interval from -0.044 to 0.036. The interval crosses zero, so the posted data are compatible with either direction of the difference. Its span also indicates that the point estimate is not highly precise: effects appreciably below or above zero remain compatible with the observed counts under the calculation used.

General statistical explanation: a confidence interval is a measure of uncertainty around an estimate, not a guarantee that the true value falls within the interval in any particular trial. Its width depends on the amount of information and the statistical method. More events or more observations can often improve precision, but the resulting precision also depends on the event frequency and design. The observed counts are limited relative to the analyzed group sizes, and the interval remains broad around the near-zero point estimate.

The confidence interval is for the unadjusted risk difference, not a reported non-inferiority analysis. The registry does not state a non-inferiority margin, so the interval cannot be judged against the trial's intended margin. It also does not report the sponsor's confidence interval or formal conclusion. The p-value of 0.851 is consistent with the lack of a clear difference in this unadjusted comparison, but it does not show equivalence or prove that the difference is clinically unimportant.

Precision is also affected by the available-follow-up analysis. The primary registry description says that participants analyzed include those with available follow-up at the specified time. Details about the number and outcomes of participants without available follow-up, and sensitivity analyses for missing data, are not reported in the registry record. Thus, the interval describes the posted calculation, while uncertainty related to missing outcome data cannot be quantified from the record.

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 illustrations based on the observed effect, not the trial's original design calculations. They are reported as participants per arm for 80% power and participants per arm for 90% power. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

For the primary comparison, planning for 100% of the observed effect gives 38,896 participants per arm for 80% power and 52,070 participants per arm for 90% power. Planning for 75% of the observed effect gives 69,969 participants per arm for 80% power and 93,668 participants per arm for 90% power. Planning for 50% of the observed effect gives 159,275 participants per arm for 80% power and 213,223 participants per arm for 90% power. These are hypothetical planning quantities, not observed trial sizes.

General explanation: power is the probability, under specified assumptions, that a study will detect a chosen effect using a stated test. The 80% and 90% columns represent different target probabilities of detecting that assumed effect; the higher target generally requires more participants. The rows use progressively smaller fractions of the observed effect. Smaller effects are harder to distinguish from random variation and therefore need more participants under the stated assumptions. These figures are not observed power.

The planning assumption of equal allocation differs from the trial's randomized 2:1 allocation. This further emphasizes that the figures are illustrations rather than a reconstruction of the trial's design. The assumptions and figures do not establish whether the original trial was adequately powered for its non-inferiority objective.

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 = 0.042; treatment proportion p₁ = 0.038; average p̄ = 0.040.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2756 = 0.5402.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2756 = 0.2320.
4. n = (0.5402 + 0.2320)² / (-0.0039)² = 38,895.6, rounded up to 38,896 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 <- 0.0415094339622641                          # control proportion
p1 <- 0.037593984962406                          # 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(1844284)
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 = 38,896 (80% power), 52,070 (90% power)
 75% of observed effect: n per arm = 69,969 (80% power), 93,668 (90% power)
 50% of observed effect: n per arm = 159,275 (80% power), 213,223 (90% power)
power.prop.test: 38895.6 
Simulated power at n = 38,896 per arm: 0.800 (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. Multiplicity, Missing Data and Analysis Populations

The registry record identifies target lesion failure at 1 year as the primary outcome and lists secondary outcomes that include DMR, TVF, and TLF in the in-hospital period. It does not report a multiplicity adjustment, a hierarchy among secondary endpoints, or a plan for interpreting multiple comparisons. This absence matters because repeated testing across outcomes can produce apparently notable results by chance. The early secondary comparisons are therefore less secure as confirmatory evidence than a single prespecified primary comparison.

The registry does not report interim analyses, stopping rules, or any adjustment for repeated looks at accumulating data. It is not possible to determine from the record whether interim monitoring was planned or performed. No assumptions about such procedures can be made from the fact that the trial is marked completed.

The primary outcome description specifies an ITT population, but also says the number analyzed includes participants with available follow-up at the relevant time. This wording makes follow-up availability part of the reported denominator. The registry record does not give a detailed account of missing primary endpoint observations, reasons for missingness, imputation, or sensitivity analyses. It also does not report how participants with incomplete follow-up were handled in other analysis populations.

For a non-inferiority trial, analysis populations and missing data can be particularly important because different approaches to deviations or missing outcomes may affect conclusions. The record does not report per-protocol results, a comparison of analysis populations, or a sensitivity analysis addressing missingness. The non-inferiority margin and formal sponsor analysis are also not reported, so neither the consequences of missing information nor the robustness of a non-inferiority conclusion can be evaluated from the registry entry.

The trial's randomization ratio and primary analysis description are available, but key statistical-plan details are not. The randomization sequence, allocation concealment, covariate adjustments, subgroup analyses, and handling of protocol deviations are not reported in the registry record. This limits reproducibility and makes the posted unadjusted comparison a descriptive summary rather than a complete account of the planned inferential analysis.

15. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: coronary artery stenosis (8.2%), coronary artery restenosis (7.9%), myocardial infarction (4.5%), angina pectoris (3.4%), coronary artery disease (3.4%).

The registry records serious adverse events in 127 of 266 participants at risk in the Absorb BVS group and 61 of 134 at risk in the XIENCE group. Other adverse events are recorded in 217 of 266 and 110 of 134 participants at risk, respectively. The registry also records 15 deaths in the Absorb BVS group and 4 in the XIENCE group. The time period and specific definition used for these death counts are not reported in the registry record.

The most frequently listed serious-event terms include coronary artery stenosis (8.2%), coronary artery restenosis (7.9%), myocardial infarction (4.5%), angina pectoris (3.4%), coronary artery disease (3.4%), and thrombosis in device (3.4%). These are registry adverse-event listings, not necessarily events judged to have been caused by a study device. The record does not report a causal attribution analysis in the information summarized.

Safety counts should be read with their denominators and definitions in mind. The at-risk group sizes differ from the primary endpoint analysis sizes, and the record does not explain the difference or specify the adverse-event observation period. These descriptive counts do not, on their own, establish a comparative safety effect. A formal comparative analysis, event timing, and details on severity and relatedness are not reported in the registry record.

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

The posted primary data describe target lesion failure in 11 of 265 participants assigned to Absorb BVS and 5 of 133 assigned to XIENCE at 1 year. The unadjusted risk difference is -0.004, and its 95% confidence interval extends from -0.044 to 0.036. The point estimate is near zero, but the interval includes both directions of difference and leaves considerable uncertainty. The p-value of 0.851 does not demonstrate equivalence.

The trial is described as a non-inferiority evaluation, but the registry record does not report the prespecified non-inferiority margin or sponsor's formal analysis. A non-inferiority conclusion depends on those details and cannot be inferred from an unadjusted p-value or a confidence interval considered without the margin. The record also does not provide a sample-size justification that can be assessed against the stated objective.

The endpoint is a composite. The posted total does not show the separate numbers for cardiac death, target vessel myocardial infarction, or ischemic-driven target lesion revascularization. Nor does it describe the timing or clinical context of each event. The secondary outcomes give some early-event information, but they use different definitions or a shorter timeframe and have few events with substantial uncertainty.

The posted comparison is also limited by the available-follow-up description. The analyzed sizes are those with endpoint follow-up, while a detailed account of missing data and sensitivity analyses is not reported in the registry record. Adverse-event counts offer descriptive safety information, but their observation period and causal attribution details are not reported. These limitations mean the registry results should be interpreted as a record of observed outcomes and an unadjusted comparison, not a complete clinical or regulatory assessment of either device.

In sum, the registry supports a narrow statistical statement: the observed TLF proportions were close in the analyzed groups, and the unadjusted estimate is imprecise. It does not establish that one device is superior, that the devices are equivalent, or that Absorb BVS met the trial's non-inferiority objective.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a test result are not enough to evaluate a non-inferiority study. The risk-difference estimate is close to zero, but its confidence interval includes effects in both directions. A non-inferiority interpretation needs a prespecified margin against which uncertainty can be judged. Because the margin and sponsor's formal analysis are not reported in the registry record, the stated design objective cannot be fully assessed from the posted comparison.

It also demonstrates how analysis denominators should be read alongside enrollment. Planned enrollment was 400, while the primary endpoint counts use 265 participants in the Absorb BVS arm and 133 in the XIENCE arm. The registry explains that analyzed participants had available follow-up at the specified time. This difference makes transparent reporting of follow-up completeness and missing-data handling important for interpreting the endpoint estimate.

The composite nature of TLF is another statistical consideration. A single count brings together cardiac death, TV-MI, and ID-TLR, but the registry does not provide component-specific primary counts. Without that breakdown, readers cannot determine which component contributes most to the composite or whether component results align with the overall estimate.

Finally, many secondary outcomes are listed, while the record does not report a multiplicity plan or secondary analyses. This creates a distinction between descriptive secondary data and confirmatory evidence. In combination, the record offers useful information about the randomization, endpoint definition, observed counts, and uncertainty, while also showing why prespecified margins, complete analysis plans, missing-data reporting, and transparent endpoint-level analyses are essential to a rigorous interpretation.

18. Limitations

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

The registry record leaves several trial-specific questions unresolved. It describes a non-inferiority design but does not report the non-inferiority margin, the original sample-size justification, or the sponsor's formal analysis of the primary outcome. Consequently, the posted unadjusted risk difference cannot establish whether the trial met its stated objective.

The primary endpoint combines cardiac death, TV-MI, and ID-TLR, but component-specific results are not reported. This limits assessment of the sources of the composite outcome. The registry also gives the analyzed endpoint sizes and says these include participants with available follow-up, but does not report missing-data counts, reasons, imputation methods, or sensitivity analyses. The effect of incomplete follow-up therefore cannot be assessed.

Important design details are absent, including the randomization sequence method, allocation concealment, the identity of the blinded parties, and detailed eligibility criteria. The registry does not report adherence, crossover, protocol deviations, or analyses of alternative populations. Such details would help readers assess implementation and understand how participants were included in the analysis.

For secondary outcomes, no reported analyses are listed, and no multiplicity strategy or hierarchy is reported. The registry does not report interim analyses or stopping rules. Adverse-event denominators are recorded, but the observation period, event relatedness, and comparative safety analysis are not described. The death counts lack a reported time period in the record.

These are limitations of what the registry record reports; they do not establish that a procedure or analysis was or was not performed. They constrain independent assessment of the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: AVJ-301 Clinical Trial: A Clinical Evaluation of AVJ-301 (Absorb™ BVS) in Japanese Population — NCT01844284.
• Registry record last updated 2020-10-08; status last verified 2019-07.
• Results first posted 2019-02-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01844284 is a completed prospective, randomized, single-blind, parallel-group, multicenter study in a Japanese population. It compared Absorb BVS with the active control XIENCE PRIME/XIENCE Xpedition and was described as a non-inferiority evaluation. Planned enrollment was 400, with randomization in a 2:1 ratio.

The primary outcome was the number of participants with target lesion failure at 1 year, defined as cardiac death, TV-MI, or ID-TLR. The posted counts are 11 of 265 for Absorb BVS and 5 of 133 for XIENCE. The unadjusted risk difference is -0.004 (95% confidence interval -0.044 to 0.036; p = 0.851). The interval reflects substantial uncertainty and does not establish equivalence or non-inferiority.

The registry also records early secondary outcomes and adverse-event counts. It does not report the non-inferiority margin, original sample-size justification, sponsor-reported primary analysis, or detailed missing-data and multiplicity methods. These omissions limit independent interpretation of whether the stated trial objective was met.