Absorb IV Randomized Controlled Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Absorb IV Randomized Controlled Trial (NCT02173379), a randomized na study. The primary outcome is Number of Participants With Target Lesion Failure (TLF).

2. Clinical Question

3. Trial Design

ABSORB IV is listed as a randomized, single-blind, parallel-group, multicenter study sponsored by Abbott Medical Devices. The registry reports an enrollment of 2,604 and describes a 1:1 allocation between Absorb BVS and XIENCE. The study began in 2014-07, reached primary completion on 2022-04-06, and is listed as completed. Its phase is recorded as NA.

The study record describes ABSORB IV as a continuation of ABSORB III under a shared protocol, because the trial designs are related. It states that data from ABSORB III and ABSORB IV would be pooled to support the ABSORB IV primary endpoint. Numerical pooled results are not reported in the registry record, so the posted arm counts should not be taken as a description of that pooled analysis.

The brief study description says the trial registered approximately 2,610 subjects from approximately 140 sites in the United States and outside the United States. The enrollment field gives 2,604. These are different kinds of registry entries: one is an approximate description in the study summary, and the other is the enrollment value recorded for the trial.

Participants were assigned to Absorb BVS or a listed XIENCE device. The registry identifies the study as single-blind but does not report which participants or study personnel were masked. It also does not report the original sample-size justification, the planned interim analyses, or the detailed statistical analysis plan. Those omissions limit how fully the design assumptions behind the sponsor’s analysis can be reconstructed from the registry record alone.

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: The number of All-Cause Mortality will differ from that reported in the Participant Flow module. This is due to the follow-up window 'treatment' of the data. Only deaths that occurred prior to the beginning of the 5-year visit window (Day 1797=1825-28) are counted in the Participant Flow; whereas in the AE table, participants who died within the follow-up window are counted.

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 30 days.

The primary endpoint counts participants with target lesion failure by 30 days. The composite includes cardiac death, myocardial infarction attributable to the target vessel, or ischemia-driven target lesion revascularization. Each component describes a different clinical event, but the composite treats a participant as having the endpoint if any qualifying component occurs. The registry does not report component-specific primary outcome counts, so the posted total cannot establish which component accounts for the observed events.

Composite endpoints are often used to capture a broader range of clinically important outcomes than a single event could capture. General statistical interpretation: combining events can make an outcome occur more often, but it can also bring together events that differ in severity or frequency. The meaning of a composite therefore depends on its definition and on the contribution of each component. In this record, those definitions are stated, while the separate component counts are not reported.

The primary outcome is presented as a participant count in an intention-to-treat population, with participants analyzed if follow-up data were available at the specified time point. The posted analysis includes 64 of 1,288 participants in the Absorb BVS arm and 48 of 1,303 in the XIENCE arm. These counts describe the registry’s 30-day outcome data; they do not, by themselves, determine the conclusion of the sponsor’s non-inferiority test.

7. Results Posted in the Registry

• XIENCE: 3.7% (48/1303) versus 5.0% (64/1288) on control; risk difference -1.3 percentage points (95% CI -2.9 to 0.3), risk ratio 0.74 (0.51–1.07); unadjusted two-proportion z-test p = 0.108.

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.

TLF at 1-year, Non-inferiority Against the Control

• 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: 6.4% (82/1272) versus 7.8% (98/1254) on control; risk difference -1.4 percentage points (95% CI -3.4 to 0.6), risk ratio 0.82 (0.62–1.09); unadjusted two-proportion z-test p = 0.181.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE and the control. The interval gives the range of effects that remain compatible with the data.

Angina at 1-year, Non-inferiority Against the Control

• 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: 39.1% (494/1265) versus 36.8% (459/1248) on control; risk difference 2.3 percentage points (95% CI -1.5 to 6.1), risk ratio 1.06 (0.96–1.17); unadjusted two-proportion z-test p = 0.240.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Acute Success- Procedural Success (Subject Level Analysis)

• 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: 95.6% (1246/1303) versus 93.1% (1194/1282) on control; risk difference 2.5 percentage points (95% CI 0.7 to 4.3), risk ratio 1.03 (1.01–1.05); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for XIENCE than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover more than one domain: target lesion failure at one year, angina at one year, procedural success during the in-hospital period, and other listed outcomes. Together, they give context beyond the 30-day primary endpoint, but they are not all measures of the same event or time horizon. Their results should therefore be interpreted outcome by outcome rather than combined into a single overall claim.

In broad terms, the posted one-year TLF analysis includes a sponsor-reported non-inferiority test, while the angina and procedural-success comparisons are presented as outcome-specific summaries. The procedures and symptoms measure different aspects of the study experience from the composite primary endpoint. Their direction and statistical evidence do not amount to a direct confirmation or refutation of the 30-day primary result. The registry does not report a unified secondary-endpoint conclusion.

General statistical explanation: multiple testing arises when many outcomes or comparisons are examined. Even when no true effect exists for any individual outcome, a larger collection of tests increases the chance that at least one result appears statistically notable by chance. Without a reported multiplicity plan, a nominal p-value for a secondary outcome should carry less weight than a result from a prespecified primary analysis. The registry record does not report whether or how multiplicity was controlled.

The record lists 168 posted secondary outcomes, so the number of results makes this caution relevant. Secondary findings can still be informative, especially when they address distinct outcomes of interest, but their precision, prespecification, and multiplicity handling matter. The available information does not establish a formal hierarchy among all secondary endpoints or whether any were intended as confirmatory. They are best treated as supporting context, not as a replacement for the primary analysis.

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

• TLF at 1-year, Non-inferiority Against the Control
• Angina at 1-year, Non-inferiority Against the Control
• Percentage of Target Lesion With Acute Success- Device Success (Lesion Level Analysis)
• Number of Participants With Acute Success- Procedural Success (Subject Level Analysis)
• Number of Death (Cardiac, Vascular, Non-cardiovascular)
• Number of Death (Cardiac, Vascular, Non-cardiovascular)
• Number of Death (Cardiac, Vascular, Non-cardiovascular)
• Number of Death (Cardiac, Vascular, Non-cardiovascular)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a binary outcome: each participant either met the composite TLF definition by 30 days or did not. The posted arm summaries give the number of participants with the event and the number analyzed. The recalculated comparison uses the event proportions in the two groups to express an absolute risk difference. The registry also includes relative measures, the risk ratio and odds ratio, but the sponsor’s reported primary analysis is a non-inferiority test rather than an ordinary test of whether the groups differ.

What does the risk difference describe?

General statistical explanation: a risk difference subtracts one group’s event proportion from the other group’s event proportion. It keeps the comparison on an absolute scale, so its value is expressed as a difference in proportions. The recalculated estimate is -0.013 for XIENCE minus Absorb BVS. A negative estimate means the observed proportion in the first group in that subtraction is lower; it does not, on its own, establish a meaningful or statistically conclusive group difference. The confidence interval gives a range of values compatible with the posted data under the calculation’s assumptions.

The risk ratio instead compares the two event proportions by division, while the odds ratio compares the odds of an event. These relative measures answer different versions of the comparison and can look numerically different from an absolute difference. The registry lists these recalculated measures, but they do not replace the sponsor’s analysis or resolve the discrepancy flagged in the record.

How is a non-inferiority test different?

General statistical explanation: a conventional superiority test commonly asks whether the data provide evidence of any difference between groups. A non-inferiority test asks whether the study can rule out a loss of effect or an increase in outcome that exceeds a prespecified margin. The test therefore depends on the chosen margin, the direction of comparison, and the statistical procedure. The registry identifies the Farrington-Manning method for the primary analysis and reports p = 0.024 at a 97.5% confidence level. The margin and estimated effect with confidence limits are not reported in the registry record.

A non-inferiority test should not be interpreted as a demonstration that the treatments are identical. General statistical explanation: it can support a claim only in relation to a specified acceptable boundary and the assumptions of the analysis. Because the margin is missing from this record, readers cannot independently judge how large a difference the sponsor regarded as acceptable. The reported analysis is still the sponsor’s registered analysis, and the flagged discrepancy means it takes precedence over a recalculation from the summary counts.

What does the unadjusted recalculation add?

The recalculation is a simple comparison based on the posted participant counts, not a recreation of the sponsor’s complete statistical model. It reports a risk difference of -0.013, a 95% confidence interval from -0.029 to 0.003, and an unadjusted p-value of 0.108. “Unadjusted” means it does not account for additional covariates or other adjustment procedures. The registry does not report enough detail to establish whether the sponsor’s analysis used further adjustments beyond the named Farrington-Manning method.

General statistical explanation: the confidence interval and p-value are related summaries, but they do not convey identical information. A confidence interval displays a range of effect estimates consistent with a specified procedure; a p-value summarizes how unusual the data would be under a null hypothesis. The interval’s inclusion of zero aligns with the unadjusted p-value not indicating a conventional difference, but that is not a test of non-inferiority and it does not supersede the sponsor’s analysis.

Why can event variability matter?

General statistical explanation: for binary outcomes, uncertainty depends partly on how many participants are analyzed and how common the event is. For other outcome types, variation can exceed what a simple model assumes; over-dispersion is one term for variability greater than the model allows. The primary endpoint is a participant event count, and the registry gives no dispersion parameter or alternative model for it. The term over-dispersion is therefore general context, not a description of a documented feature of this primary analysis.

The registry lists a large number of outcome measures and two reported analyses overall, while 168 secondary outcomes are posted. This makes it especially important to distinguish a prespecified primary test from exploratory or multiple secondary comparisons. The multiplicity strategy and full analysis plan are not reported in the registry record. The individual p-values should therefore be read as outcome-specific results rather than as a complete, multiplicity-controlled set of conclusions.

11. Confidence Intervals and Precision

The recalculated 30-day risk difference is -0.013, with a 95% confidence interval from -0.029 to 0.003. The interval includes zero and extends from negative values to a small positive value. This means the recalculated data are compatible with more than one direction of difference, under the assumptions of that calculation. Its width also signals that the point estimate should not be treated as an exact measure of the underlying difference.

General statistical explanation: a confidence interval reflects sampling uncertainty under the method used to construct it. A 95% confidence interval is not a guarantee that the true value lies in that particular interval, and it does not account automatically for bias, missing data, unreported design choices, or selective analysis. It describes precision within the calculation’s assumptions, not every source of uncertainty in the trial.

The sponsor’s non-inferiority analysis uses a 97.5% confidence level, but the registry does not report its confidence limits or effect estimate. The value p = 0.024 is reported for the Farrington-Manning test. Without the margin and confidence limits, the sponsor result cannot be fully assessed for magnitude or precision from the registry record. The unadjusted 95% interval should not be substituted for that non-inferiority interval.

Analysis counts are 1,288 for Absorb BVS and 1,303 for XIENCE for the primary endpoint. The registry says the analyzed count includes participants with available follow-up data at that time point. It does not report the reasons for unavailable data or the handling of missing outcomes in greater detail. That limits interpretation of precision because the confidence interval reflects the analyzed counts, while the record does not establish whether those with unavailable follow-up differ from those analyzed.

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 illustrations express required sample sizes as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The calculation uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, or 50% of that observed effect. The trial’s original design assumptions are not reported in the registry record.

Power is the chance that a planned study would detect an effect of the size specified by the planning scenario, if that effect were present and the calculation assumptions held. General statistical explanation: a design targeting 90% power has a higher chance of detecting the specified effect than one targeting 80% power, and generally requires more participants. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. The displayed values illustrate that pattern across the listed scenarios.

For the primary endpoint, the figures are 3,934 and 5,265 participants per arm for planning at 100% of the observed effect, 7,241 and 9,693 for 75%, and 16,848 and 22,554 for 50%, for the 80% and 90% power targets respectively. These are planning illustrations calculated from the observed effect, not the actual enrollment target or a report of the trial’s design calculation. They are not observed power: observed data cannot establish the probability that the completed trial had to detect the effect it happened to observe.

These calculations do not reproduce the sponsor’s non-inferiority design. In particular, the original margin and sample-size assumptions are not reported in the registry record, and the simple planning assumptions do not include a non-inferiority margin. The values should be read as hypothetical planning references, not as a reassessment of whether the completed trial was adequately designed.

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 = 0.050; treatment proportion p₁ = 0.037; average p̄ = 0.043.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2877 = 0.5639.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2876 = 0.2420.
4. n = (0.5639 + 0.2420)² / (-0.0129)² = 3,933.0, rounded up to 3,934 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 <- 0.0496894409937888                          # control proportion
p1 <- 0.0368380660015349                          # 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(2173379)
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 = 3,934 (80% power), 5,265 (90% power)
 75% of observed effect: n per arm = 7,241 (80% power), 9,693 (90% power)
 50% of observed effect: n per arm = 16,848 (80% power), 22,554 (90% power)
power.prop.test: 3933 
Simulated power at n = 3,934 per arm: 0.799 (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 is reported as a Farrington-Manning non-inferiority test, with p = 0.024 and a 97.5% confidence level. The registry does not include the corresponding effect estimate, confidence limits, or non-inferiority margin. Those omissions prevent an independent reconstruction of the sponsor’s decision rule from this record alone.

The unadjusted recalculation from the posted primary counts gives a risk difference of -0.013, with a 95% confidence interval from -0.029 to 0.003 and p = 0.108. This calculation addresses an unadjusted comparison from summary counts, not the sponsor’s non-inferiority question. The registry flags a discrepancy between the sponsor analysis and the recalculation. In that situation, the sponsor’s own analysis takes precedence; the recalculation is useful as a check on the posted counts, but it is not a substitute for the registered analysis.

A non-inferiority p-value must be interpreted with the prespecified margin and its direction. General statistical explanation: the margin defines the boundary beyond which an outcome difference would be considered too large for the non-inferiority claim. Since that boundary is not reported, the p-value cannot be translated into a full assessment of the clinical threshold used. The record also does not report enough detail to explain the discrepancy, so its source should not be guessed.

15. Multiplicity, Missing Data and Analysis Populations

The record identifies a primary endpoint and a large set of secondary outcomes, but it does not report a multiplicity adjustment plan. It also does not report a hierarchy for testing secondary outcomes, the distinction between confirmatory and exploratory analyses, or how decisions were made across the many posted endpoints. Without those details, nominal secondary p-values cannot be interpreted as if they were necessarily protected against the risk of false-positive findings from multiple testing.

The primary outcome is described as an intention-to-treat population, with the analyzed count including participants with available follow-up at the specified time point. This description does not give a complete account of missing-data handling. Reasons for unavailable outcome data, imputation procedures, sensitivity analyses, or a detailed approach to participants who did not have follow-up are not reported in the registry record. The enrolled total and endpoint analysis counts are not identical, but the record does not explain the difference in detail.

Analysis denominators also vary across posted outcomes. That may reflect the stated time point and availability of outcome data, but the registry does not report enough information to determine all reasons for those variations. The analysis population definition is not repeated in full for every secondary outcome. As a result, comparisons across endpoints may involve different analyzed participants, and the record does not permit a complete assessment of the impact of that variation.

The original sample-size justification and the sponsor’s full statistical analysis plan are not reported in the registry record. Interim analyses, stopping rules, and any associated adjustment to statistical thresholds are also not reported. These omissions do not establish that such procedures were absent; they mean that the record does not document them. The sponsor’s primary non-inferiority test is identified by method and p-value, but the non-inferiority margin and its confidence limits are absent. Those missing details constrain an independent appraisal of the primary test as well as the secondary testing framework.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (10.4%), non-cardiac chest pain (6.3%), myocardial infarction (5.2%), angina unstable (4.4%), atrial fibrillation (3.5%).

The registry reports serious adverse events affecting 827 of 1,296 participants at risk in the Absorb BVS group and 774 of 1,308 at risk in the XIENCE group. For other adverse events, the listed counts are 1,012 of 1,296 and 1,034 of 1,308, respectively. Death counts are 77 for Absorb BVS and 72 for XIENCE. These are registry-reported counts and denominators; they are not the primary efficacy endpoint.

The most frequently listed serious adverse event terms include angina pectoris, non-cardiac chest pain, myocardial infarction, unstable angina, atrial fibrillation, and coronary artery disease. Their reported percentages are event-term entries in the registry. The record does not provide enough detail to determine from these entries whether events were adjudicated, whether participants could contribute more than one term, or how each term maps to unique participants.

These summaries do not establish that a device caused an adverse event or that one group had a definitive safety advantage. Comparative safety interpretation would require attention to event definitions, timing, follow-up, exposure, and analysis methods. Further detail about those matters is not reported in the registry record.

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

The posted primary summaries show 64 participants with target lesion failure among 1,288 analyzed in the Absorb BVS arm and 48 among 1,303 analyzed in the XIENCE arm at 30 days. The unadjusted recalculation estimates a risk difference of -0.013 for XIENCE minus Absorb BVS, with a 95% confidence interval from -0.029 to 0.003. That interval includes zero and represents uncertainty around an unadjusted comparison of the posted counts.

The sponsor reports a different analysis: a Farrington-Manning non-inferiority test with p = 0.024 and a 97.5% confidence level. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence over the simple recalculation. At the same time, the record does not report the non-inferiority margin or the sponsor’s confidence limits. Readers therefore cannot fully evaluate the threshold or estimate magnitude from the posted registry information alone.

General statistical explanation: a non-inferiority finding does not mean that two treatments have identical effects. It concerns whether the data rule out a difference beyond a specified boundary. That boundary is central to interpretation, and it is not reported. Likewise, a p-value is not the probability that the null hypothesis is true, nor is it a direct measure of clinical importance.

The results do not, by themselves, establish the separate contribution of cardiac death, target-vessel myocardial infarction, or ischemia-driven target lesion revascularization to the composite. The record also does not fully describe missing-data handling, the multiplicity plan, or the original sample-size assumptions. Secondary outcomes address other time points and domains and should not be used as substitutes for the primary analysis. Safety counts are descriptive registry entries and do not by themselves demonstrate a causal relationship.

In short, the posted counts and recalculation describe the observed primary outcome and its unadjusted uncertainty, while the registered sponsor analysis addresses non-inferiority. Those analyses answer related but distinct statistical questions. The registry record leaves key details needed for a fully independent interpretation unreported.

18. Why This Trial Matters Statistically

This trial is statistically notable because its stated primary question is non-inferiority, while the registry also permits a straightforward recalculation from the arm-level participant counts. Comparing the two makes clear why the analysis method and test question matter: an unadjusted comparison of event proportions is not interchangeable with a non-inferiority test that depends on a margin.

The registry identifies the sponsor’s Farrington-Manning method and reports a p-value at a 97.5% confidence level. Yet the margin and confidence limits are not reported, and the record flags a discrepancy between the sponsor analysis and the recalculation. This combination illustrates an important reporting principle: a method name and p-value do not always give enough information to assess the magnitude or practical threshold of a result.

The trial also reports a composite endpoint and a range of secondary outcomes across time points and clinical domains. General statistical explanation: such breadth can help describe multiple dimensions of a study, but it also makes prespecification and multiplicity handling important. With many outcomes, isolated nominal results deserve cautious interpretation unless the testing strategy is clear.

Finally, outcome-specific analyzed counts reflect available follow-up, according to the registry description. Understanding how missing outcome data were handled, how the pooled trial question was analyzed, and how the original sample size was justified would help readers assess precision and robustness. Those details are not reported in the registry record. The case therefore highlights both the value of transparent registry reporting and the limits of interpreting a result when essential analysis details are absent.

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 primary sponsor analysis cannot be fully reconstructed from the registry record. Although it identifies the Farrington-Manning non-inferiority method, reports p = 0.024, and gives a 97.5% confidence level, it does not report the non-inferiority margin, effect estimate, or confidence limits. The record flags a discrepancy with the unadjusted recalculation but does not explain its source. The sponsor’s own analysis takes precedence, but these missing details restrict independent assessment.

The record states that ABSORB III and ABSORB IV data would be pooled to support the ABSORB IV primary endpoint. It does not report numerical pooled results or explain how the posted trial-level summaries relate to that pooled analysis. The enrollment field and approximate enrollment description also differ in form, and the record does not give additional detail to reconcile them.

For the primary outcome, analysis is limited to participants with available follow-up at the relevant time point. The record does not describe reasons for missing follow-up, imputation, or sensitivity analyses. The exact masking roles are not reported despite the single-blind designation. The original sample-size justification, interim analyses, and full analysis plan are also not reported.

The primary composite combines three event types, but separate component counts are not reported. The serious adverse event summaries include affected counts and common terms, but the record does not fully explain event-level versus participant-level overlap or provide detailed adjudication information. Finally, the multiplicity strategy across the many secondary outcomes is not reported, which limits the confirmatory interpretation of isolated secondary findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Absorb IV Randomized Controlled Trial — NCT02173379.
• Registry record last updated 2023-10-30; status last verified 2023-10.
• Results first posted 2018-07-24.
• 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

NCT02173379, the Absorb IV Randomized Controlled Trial, is listed as a completed, randomized, single-blind, parallel-group study sponsored by Abbott Medical Devices. The registry records 2,604 enrolled participants and describes a 1:1 comparison of Absorb BVS with XIENCE. The primary endpoint is the number of participants with TLF at 30 days, defined as a composite of cardiac death, target-vessel myocardial infarction, or ischemia-driven target lesion revascularization.

The posted primary counts are 64 of 1,288 for Absorb BVS and 48 of 1,303 for XIENCE. The sponsor reports a Farrington-Manning non-inferiority analysis with p = 0.024 at a 97.5% confidence level. An unadjusted recalculation yields a risk difference of -0.013, with a 95% confidence interval from -0.029 to 0.003 and p = 0.108. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence.

The non-inferiority margin, pooled outcome results, detailed missing-data procedures, multiplicity plan, original sample-size justification, and full statistical analysis plan are not reported in the registry record. These omissions limit independent evaluation of the analysis and its precision.