Randomized Trial of IN.PACT Admiral® Drug Coated Balloon vs Standard PTA for the Treatment of SFA and Proximal Popliteal Arterial Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Trial of IN.PACT Admiral® Drug Coated Balloon vs Standard PTA for the Treatment of SFA and Proximal Popliteal Arterial Disease (NCT01175850), a randomized na study. The primary outcome is Primary Patency.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group device trial with no masking. It compares IN.PACT Admiral drug-coated balloon angioplasty with standard percutaneous transluminal angioplasty using a non-drug-coated balloon. The study enrolled 331 participants with peripheral arterial disease and is marked completed. The listed start was 2010-09, and the listed primary completion was 2014-02.

The intervention combined the mechanical dilation effect of a PTA balloon with paclitaxel released from the balloon surface into the vessel wall. The stated intention of that drug absorption was to limit the chances and extent of arterial re-narrowing over time. The comparison intervention was standard balloon angioplasty without the drug coating. The registry describes both groups as receiving balloon angioplasty.

The primary endpoint was measured at 12 Month. Its definition combines freedom from clinically driven target lesion revascularization with freedom from restenosis measured using duplex ultrasound and a peak systolic velocity ratio threshold. This makes the endpoint a binary participant-level outcome: each participant with evaluable data is classified according to whether the defined patency outcome was met.

The primary endpoint description names an intention-to-treat population of 331, while also stating that subjects without evaluable data at the reporting timeframe are excluded. The displayed primary endpoint counts are 191 in the drug-coated balloon group and 103 in the standard PTA group. The record does not explain the relationship between the population description and those endpoint counts. It also does not report the original sample-size justification, detailed allocation procedures, or the protocol's planned statistical analysis beyond the posted analysis information.

The registry lists 19 outcome measures and 19 analyses. Secondary outcomes include major adverse events, all-cause death, target-vessel and target-lesion revascularization, time to first clinically driven target-lesion revascularization, major target-limb amputation, thrombosis at the target lesion, and primary sustained clinical improvement. The detailed secondary results available in the record cover only some of these outcomes; results for the remaining measures are not reported in the registry record.

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 IN.PACT SFA Trial was designed as a two-phase randomized trial. IN.PACT SFA I, the first phase was conducted in Europe with 150 subjects enrolled. IN.PACT SFA II, the second phase, was conducted in the US with 181 subjects enrolled. The data from both phases of the IN.PACT SFA Trial have been pooled and comprise the pivotal trial data.

IN.PACT SFA I Phase

IN.PACT SFA II Phase

Analysis population for the primary outcome, as defined in the registry: Intention-to-Treat (ITT) (n=331) that excludes subjects who did not have evaluable data at the reporting timeframe.

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 Primary Patency, measured over 12 Month.

Primary patency is the trial's primary endpoint at 12 Month. In the registry definition, a participant has primary patency if there is freedom from clinically driven target lesion revascularization or restenosis, with restenosis assessed by duplex ultrasound peak systolic velocity ratio ≤ 2.4. Thus, the endpoint combines a clinical event—returning for a target-lesion procedure because it is clinically indicated—with an imaging-based measure of narrowing. It is reported as a percentage of participants.

This kind of combined endpoint is used to capture more than one way that a treated artery may lose patency during follow-up. A repeat procedure and an imaging finding are different forms of evidence, so the definition makes explicit which clinical and ultrasound criteria count toward the endpoint. The measure does not describe the severity of every individual event, the timing of an event within the follow-up period, or outcomes beyond the stated assessment timeframe.

At 12 Month, the registry reports primary patency of 82.2% in the drug-coated balloon group and 52.4% in the standard PTA group. The endpoint population description excludes subjects without evaluable data at the reporting timeframe, even though it is labeled intention-to-treat. The registry record does not provide further detail about how unevaluable participants were handled or how the endpoint was adjudicated.

7. Results Posted in the Registry

• Drug-Coated Balloon (DCB): 82.2% (157/191) versus 52.4% (54/103) on control; risk difference 29.8 percentage points (95% CI 18.7 to 40.8), risk ratio 1.57 (1.29–1.91); unadjusted two-proportion z-test p = <0.001.

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.

All-cause Death

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Drug-Coated Balloon (DCB): 1.9% (4/207) versus 0.0% (0/107) on control; risk difference 1.9 percentage points (95% CI 0.1 to 3.8); unadjusted two-proportion z-test p = 0.148.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Drug-Coated Balloon (DCB) and the control. The interval gives the range of effects that remain compatible with the data.

Target Vessel Revascularization (TVR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Drug-Coated Balloon (DCB): 4.8% (10/207) versus 23.4% (25/107) on control; risk difference -18.5 percentage points (95% CI -27.1 to -10.0), risk ratio 0.21 (0.10–0.41); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Drug-Coated Balloon (DCB) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Target Lesion Revascularization (TLR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Drug-Coated Balloon (DCB): 2.9% (6/207) versus 20.6% (22/107) on control; risk difference -17.7 percentage points (95% CI -25.7 to -9.7), risk ratio 0.14 (0.06–0.34); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Drug-Coated Balloon (DCB) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span safety events, death, and further procedures related to the treated vessel or lesion. The detailed results available for target-vessel and target-lesion revascularization follow a pattern consistent in direction with the primary patency result. The available all-cause death result does not show the same statistical pattern, and its low event count limits the information it can provide about differences between groups.

These outcomes are related to, but not interchangeable with, primary patency. Revascularization is one type of event relevant to loss of patency, while the primary definition also includes restenosis by ultrasound criteria. Death is a distinct outcome and is not a measure of vessel patency. Differences in endpoint definitions and assessment populations mean that agreement or disagreement across outcomes should be interpreted cautiously rather than treated as a direct replication or contradiction.

The registry identifies 19 outcome measures and 19 analyses, but detailed data for only some secondary outcomes are available in the record. The remaining detailed results are not reported in the registry record. The existence of a listed endpoint does not establish its result, so no conclusions about those outcomes can be drawn from their titles alone.

Secondary analyses generally carry less inferential weight when many endpoints are examined without a reported multiplicity strategy. A small unadjusted p-value may be informative, but multiple testing increases the chance of observing a notable result by chance across the outcome family. The registry record does not report adjustment for multiplicity or identify a confirmatory hierarchy for secondary outcomes. These results can add context to the primary finding, but they should not be treated as independent confirmation of it or as definitive evidence for every secondary claim.

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

• Major Adverse Events (MAE) Composite
• All-cause Death
• Target Vessel Revascularization (TVR)
• Target Lesion Revascularization (TLR)
• Time to First Clinically Driven Target Lesion Revascularization (CD-TLR)
• Major Target Limb Amputation
• Thrombosis at the Target Lesion
• Primary Sustained Clinical Improvement

9. Statistical Interpretation

10. Statistical Methods Explained

What does a binary endpoint represent?

A binary endpoint places each participant into one of two outcome categories, such as meeting or not meeting a defined patency criterion. The registry reports the primary outcome as a percentage of participants. For this trial, the definition counts freedom from clinically driven target lesion revascularization or restenosis by the stated duplex ultrasound criterion as primary patency. A percentage is therefore a summary of how often the defined outcome was observed among participants included in that endpoint result. It is not a measurement of the amount of narrowing or a summary of the timing of events.

For a binary outcome, the number of participants with the event and the number assessed matter alongside the percentage. The primary endpoint arm counts are 191 and 103. The endpoint description also gives an intention-to-treat population of 331 while saying that participants without evaluable data are excluded. Since the record does not explain that distinction, readers should not assume that all enrolled participants contributed to the endpoint percentages.

What does the risk difference describe?

The risk difference compares the outcome probabilities in two groups by subtracting one group probability from the other. Its value is expressed on an absolute scale, which makes it different from a risk ratio or odds ratio. The recalculated primary risk difference is 0.298, and its confidence interval extends from 0.187 to 0.408. The order of the comparison is drug-coated balloon relative to standard PTA, so a positive value corresponds to a higher reported primary patency proportion in the drug-coated balloon group.

A risk difference is useful for conveying the absolute separation in group rates, but it is tied to the chosen outcome definition and follow-up time. It does not describe outcomes after 12 Month, nor does it adjust for covariates. The posted calculation is unadjusted; no adjusted effect estimate is reported in the registry record.

How should the reported test and p-value be read?

The registry reports a Z-test for the primary comparison and gives p < 0.001. A p-value describes how incompatible the observed data are with a statistical null model of no group difference, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not quantify the clinical importance of the result. The recalculated unadjusted comparison also has p < 0.001. A test result is best read together with the estimated effect and its interval, rather than as a stand-alone verdict.

The record does not give the full specification of the Z-test or say whether the sponsor analysis adjusted for any other variables. The posted test is therefore the principal registry-reported inferential result, while the recalculated risk difference and interval are an unadjusted summary based on the posted group counts and percentages.

Why use a confidence interval?

A confidence interval describes the range of effect estimates reasonably compatible with the data and the method used to calculate it. It communicates uncertainty in a way that a single point estimate cannot. For the primary endpoint, the interval is entirely above zero, indicating that the unadjusted data are compatible with a positive risk difference across the reported interval. The interval does not resolve questions about missing outcome data, measurement, or whether the finding generalizes beyond this trial.

Interval width is influenced by the amount of information in the data and by the variability of the outcome. More observations can often improve precision, but the actual precision also depends on the event proportions and the calculation method. No confidence level is specified for the recalculated intervals in the registry record, so the interval should be understood as the posted recalculation rather than attributed a confidence level not recorded there.

Why can secondary outcomes be less conclusive?

Secondary endpoints may address different aspects of safety or effectiveness, but each creates another opportunity to observe an apparently notable result by chance when many outcomes are tested. A multiplicity procedure can control the overall false-positive risk across a family of tests, but the registry record does not report such a procedure. Consequently, unadjusted secondary p-values should be considered exploratory or supportive rather than treated as a series of independent confirmations. This qualification does not alter the individual numbers; it affects how much inferential weight to place on them collectively.

Outcome definitions and denominators also vary. The primary patency endpoint uses its own definition and evaluable population, while secondary outcomes have their own listed denominators and assessment descriptions. A comparison should be interpreted using the population and timeframe attached to that outcome, rather than assuming that all analyses include the same participants.

11. Confidence Intervals and Precision

The primary endpoint result is 82.2% for the drug-coated balloon group and 52.4% for standard PTA. The recalculated unadjusted risk difference is 0.298, with a confidence interval from 0.187 to 0.408. The estimate is a single summary of the group separation; the interval communicates that the underlying difference is not known with perfect precision. Because both interval limits are positive, the interval does not include zero under the recalculation method.

A confidence interval is not a guarantee that the true effect lies within its limits, nor is it a range of individual participant outcomes. It describes uncertainty in an estimated group-level effect under a statistical method. The registry record does not specify the confidence level for this recalculated interval, so no confidence level should be inferred from the record. The sponsor's reported primary analysis gives a p-value but does not report an effect estimate or interval.

Precision depends in part on the information available for the analysis. The primary endpoint arm counts are 191 and 103, while the population description says that participants without evaluable data at the reporting timeframe are excluded from the stated intention-to-treat population. The record does not clarify the relationship between these figures. This limits assessment of how missing or unevaluable observations may affect the endpoint estimate.

The confidence interval describes the primary endpoint risk difference, not the full range of possible results in other populations, at other timeframes, or under different endpoint definitions. It also does not account for unreported sources of bias or uncertainty, such as outcome assessment procedures. The trial's unmasked design and the registry's limited description of missing-data handling are relevant when considering what the numerical precision can and cannot convey.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's own design calculations. For these binary outcomes, the figures are participants per arm. They are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

The columns for 80% and 90% power describe the number of participants per arm needed, under those assumptions, for a study to have the corresponding chance of detecting the specified effect if that effect is the true one. The planning rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For the primary endpoint, the listed requirements are 38 and 51 participants per arm when planning for 100% of the observed effect; 72 and 96 when planning for 75%; and 170 and 226 when planning for 50%, for 80% and 90% power respectively.

Smaller effects are harder to distinguish from random variation, so they require more participants for the same target power under the stated assumptions. The figures are not observed power and do not describe the probability that the trial's result is true. They are illustrations derived from the observed estimate, which may itself be uncertain. They should not be mistaken for the original trial's enrollment target or sample-size justification; those original design assumptions are not reported in the registry record.

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 = 0.524; treatment proportion p₁ = 0.822; average p̄ = 0.673.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6634 = 1.3002.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6291 = 0.5294.
4. n = (1.3002 + 0.5294)² / (0.2977)² = 37.8, rounded up to 38 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 <- 0.524271844660194                          # control proportion
p1 <- 0.821989528795812                          # 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(1175850)
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 (80% power), 51 (90% power)
 75% of observed effect: n per arm = 72 (80% power), 96 (90% power)
 50% of observed effect: n per arm = 170 (80% power), 226 (90% power)
power.prop.test: 37.8 
Simulated power at n = 38 per arm: 0.810 (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 own primary analysis is reported as a Z-test, with p < 0.001. The recalculated primary comparison is an unadjusted risk difference of 0.298, with a confidence interval from 0.187 to 0.408 and p < 0.001. Both summaries indicate a difference between the groups in the primary endpoint data, but they present different statistical information: the registry-reported test gives a p-value, while the recalculation provides an absolute effect estimate and an interval.

The registry record does not provide the sponsor's primary effect estimate or confidence interval, nor the full details of the Z-test. The recalculation uses posted summary statistics and is unadjusted; it is not a substitute for the sponsor's complete analysis. The record marks no discrepancy between the available sponsor and recalculated primary findings. The sponsor's reported analysis remains the trial's own analysis, while the recalculation offers a transparent, simple comparison of the posted rates.

For secondary outcomes, the sponsor reports Chi-squared tests. Those analyses and the unadjusted recalculations do not always give the same inferential summary. For example, the reported all-cause death test has p = 0.926, while the simple unadjusted recalculation has p = 0.148. That contrast underscores why the sponsor's own analysis should be distinguished from a recalculation based on summary counts, particularly when the record does not give the full analysis specifications.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 19 outcome measures and 19 analyses. Examining many outcomes raises a multiplicity issue: when several statistical tests are conducted, the chance of at least one apparently unusual result can increase even if no true differences exist. Statistical procedures can address this by adjusting thresholds or estimates across a defined family of outcomes. The registry record does not report whether any multiplicity adjustment was planned or applied, or whether secondary endpoints followed a prespecified hierarchy.

This matters most when interpreting the secondary p-values. The reported primary test is clearly identified as the primary endpoint analysis, but the record does not state how the sponsor distinguished confirmatory from exploratory secondary analyses. The secondary results should therefore be read as outcome-specific evidence, with appropriate caution about the broader set of analyses, rather than as a set of independent tests each carrying the same weight as the primary comparison.

The primary endpoint description states that the intention-to-treat population is n=331 and excludes subjects who did not have evaluable data at the reporting timeframe. The posted primary arm counts are 191 and 103. These figures are not reconciled in the registry record. The record does not report how many participants lacked evaluable primary outcome data, how missing observations were handled, whether imputation was used, or whether sensitivity analyses were performed. It also does not report enough detail to determine how the stated intention-to-treat label was operationalized.

Secondary endpoints have their own denominators, and these do not necessarily match the primary endpoint counts. The record does not explain all denominator differences or give a full account of participant flow for each analysis. Without that information, readers cannot fully assess whether missingness or differences in analysis populations may affect comparisons across outcomes.

Randomization supports a planned comparison between groups, but it does not eliminate concerns arising from missing endpoint data, measurement, or analysis choices. The registry record does not report the original protocol's detailed statistical plan, its missing-data strategy, interim analyses, or the sample-size justification. Those features should not be inferred from the posted results.

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: intermittent claudication (9.9%), femoral arterial stenosis (9.0%), femoral artery dissection (4.5%), femoral artery occlusion (4.5%), peripheral arterial occlusive disease (4.5%).

The serious adverse event figures list 220 participants at risk in the drug-coated balloon group, with 102 affected, and 111 at risk in the standard PTA group, with 62 affected. The other adverse event figures list 220 at risk and 104 affected in the drug-coated balloon group, and 111 at risk and 62 affected in the standard PTA group. These are the registry's group counts; they are not estimates of comparative risk adjusted for differences between participants.

The registry also lists serious adverse event terms with percentages: Intermittent Claudication, 9.9%; Femoral Arterial Stenosis, 9.0%; Femoral Artery Dissection, 4.5%; Femoral Artery Occlusion, 4.5%; Peripheral Arterial Occlusive Disease, 4.5%; and Arterial Restenosis, 3.6%. The record does not give group-specific counts for these listed terms in the data, so they should not be attributed to one treatment group.

Deaths are not populated in the adverse-event summary fields. All-cause death is separately listed as a 12-month secondary outcome. The serious-event counts describe the recorded safety experience, but without additional detail on event definitions, severity grading, relatedness, follow-up completeness, or participant-level overlap, they do not by themselves establish comparative safety.

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

The posted data show a higher primary patency percentage in the drug-coated balloon group than in the standard PTA group at 12 Month. The recalculated unadjusted risk difference is positive, and its confidence interval does not include zero. The sponsor's reported primary test also gives p < 0.001. Taken together, these statistics indicate a difference in the recorded primary outcome between the randomized groups in this trial.

That finding is specific to the registry definition of primary patency, the participants with evaluable outcome data, and the stated follow-up assessment. It combines absence of clinically driven target lesion revascularization with an ultrasound criterion. It is not a direct measure of every aspect of a participant's health, does not describe outcomes beyond the reported timeframe, and does not settle whether the observed difference is important to an individual patient or applicable in other settings.

The results do not establish that the intervention works or does not work in every population, nor do they answer questions about long-term outcomes not reported in the registry. The unmasked trial design, the unresolved endpoint denominator description, and the absence of detailed missing-data information limit how completely the posted estimate can be interpreted. The registry also does not report the original protocol's full statistical plan or its sample-size justification.

Secondary results add context but should not be made to carry more weight than the record supports. Revascularization outcomes are related to patency, while death and other safety outcomes address different questions. Multiple outcome analyses without a reported adjustment strategy also make unadjusted secondary findings less conclusive. The available results are evidence about the outcomes recorded in this trial, not a complete account of every possible benefit, harm, or longer-term effect.

18. Why This Trial Matters Statistically

This trial illustrates how an endpoint definition determines what a statistical comparison means. Primary patency is not simply a report of whether the artery remained open on imaging; the registry combines an ultrasound-based restenosis criterion with freedom from clinically driven target lesion revascularization. The resulting binary outcome makes a clear group comparison possible, but readers need to understand both parts of its definition to interpret the estimate.

The primary result also illustrates the distinction between a p-value and an effect estimate. The sponsor reports a Z-test p-value, while the unadjusted recalculation gives an absolute risk difference and confidence interval. The p-value addresses compatibility with a null model; the effect estimate and interval describe the size and precision of the group contrast. Neither alone provides a complete account of clinical relevance or the result's limitations.

Denominator transparency matters as much as the comparison itself. The registry describes an intention-to-treat population of 331 while excluding participants without evaluable data at the reporting timeframe, and it gives primary endpoint arm counts of 191 and 103. Because the record does not reconcile those details, readers cannot fully reconstruct the endpoint population. This is a practical reminder that the label attached to an analysis does not replace clear reporting of who contributed data.

Finally, multiple secondary outcomes create an interpretive challenge. A coherent pattern across related outcomes can be informative, but unadjusted tests do not automatically provide separate confirmatory evidence. The absence of a reported multiplicity strategy and a complete analysis plan limits what can be concluded from the broader set of analyses. Statistical interpretation depends on the outcome definition, analysis population, uncertainty, and reporting context together.

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 trial was unmasked. Knowledge of group assignment can be relevant to outcome ascertainment or decisions about clinically driven procedures, although the registry record does not report whether or how such processes were protected from influence. Primary patency includes a clinically driven revascularization component as well as an imaging-based restenosis criterion, so the endpoint combines different forms of assessment.

The primary endpoint population description is difficult to reconcile with the reported arm counts. It names an intention-to-treat population of 331 while excluding participants without evaluable data at the reporting timeframe; the reported arm counts are 191 and 103. The registry record does not explain this wording, provide participant flow for the primary analysis, or describe missing-data handling. This limits independent assessment of the outcome denominators.

The primary outcome is reported at 12 Month. Results for follow-up beyond that timeframe are not reported in the registry record. Although 19 outcome measures and 19 analyses are listed, detailed results are not available for all of them. No multiplicity strategy is reported, limiting the strength of conclusions drawn from secondary analyses.

The registry does not report the original sample-size justification, a full statistical analysis plan, interim analyses, or detailed analysis procedures for the sponsor's tests. It also does not provide group-specific counts for the listed serious adverse event terms. The adverse event summary lacks some information needed for a fuller comparative safety assessment, including event-relatedness details and a clear account of participant-level overlap. These reporting gaps do not negate the posted results, but they constrain how much can be reconstructed from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Randomized Trial of IN.PACT Admiral® Drug Coated Balloon vs Standard PTA for the Treatment of SFA and Proximal Popliteal Arterial Disease — NCT01175850.
• Registry record last updated 2017-05-16; status last verified 2017-04.
• Results first posted 2015-10-06.
• 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.

23. Record Summary

NCT01175850 is a completed randomized, parallel-group trial sponsored by Medtronic Endovascular. It compared IN.PACT Admiral drug-coated balloon angioplasty with standard PTA balloon angioplasty for peripheral arterial disease involving the SFA and proximal popliteal artery. The trial enrolled 331 participants and had no masking.

The primary outcome was 12-month primary patency, defined by freedom from clinically driven target lesion revascularization or restenosis by duplex ultrasound peak systolic velocity ratio ≤ 2.4. The registry reports primary patency of 82.2% for the drug-coated balloon group and 52.4% for standard PTA; its reported primary comparison used a Z-test and gave p < 0.001.

Secondary outcomes cover revascularization, death, other clinical events, and safety. Detailed results are available for only some outcomes. The record does not reconcile the primary endpoint population description with its arm counts, and it does not report the original sample-size justification, full statistical plan, missing-data procedures, or a multiplicity strategy.