A Clinical Evaluation of the MicroSTent® PeripherAl Vascular SteNt in Subjects With Arterial Disease Below the Knee (STAND): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Clinical Evaluation of the MicroSTent® PeripherAl Vascular SteNt in Subjects With Arterial Disease Below the Knee (STAND) (NCT03477604), a randomized na study. The primary outcome is Number of Subjects With Patency of the Target Lesion.

2. Clinical Question

3. Trial Design

STAND is a randomized, multicenter clinical trial with a parallel-group design. It compares PTA plus the MicroStent peripheral vascular stent system with PTA alone for treatment of infrapopliteal lesions in people with peripheral arterial disease. The registry lists the phase as NA and masking as none. The study began on 2020-03-31, has a primary completion date of 2025-06-05, and is listed as active, not recruiting. The recorded enrollment is 177.

The trial’s two arms differ by the addition of the MicroStent system to PTA in the intervention arm. The registry describes implantation of the stent for treatment of arterial lesions below the knee. The standard-PTA arm is named as the comparator, but its arm description is blank in the record. The registry does not report further details about procedural standardization, treatment adherence, crossovers, or follow-up procedures.

The primary endpoint is assessed up to 6 months after randomization. The registry’s population description gives mITT counts of 117 for the MicroStent arm and 59 for the PTA arm. It separately states that 99 and 55 participants were the overall numbers analyzed at 6 months. The posted primary outcome counts use denominators of 99 and 51. These different counts are all retained as described in the registry record; the available information does not explain the difference between the stated six-month overall counts and the denominators used for the posted outcome comparison.

Randomization can help make a comparison between assigned groups interpretable, but the registry record does not report the sequence-generation procedure, concealment approach, or detailed analysis plan. The trial is unmasked, so participants and study personnel were not described as masked. No formal analysis listings are 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: 117 subjects in the MicroStent and 59 subjects with PTA were included in the Intent to Treat (mITT) population. At 6 months 99 subjects in the Microstent arm and 55 subjects in the PTA arm were the overall number of participants analyzed.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Intent to treat population

6. Primary Endpoint

The registry lists the primary outcome as Number of Subjects With Patency of the Target Lesion, measured over up to 6 months after randomization.

The primary endpoint counts participants with target-lesion patency up to 6 months after randomization. The registry defines patency as freedom from target-lesion occlusion without clinically driven reintervention at the target lesion or major amputation. It is therefore a binary participant-level outcome: each analyzed participant either met the stated patency definition or did not.

This endpoint is used to capture whether the treated lesion remains open without a clinically driven repeat procedure or major amputation during the stated follow-up period. Combining those components gives the endpoint a clinical and procedural interpretation, but it also means that the count does not isolate which component accounts for a participant not meeting the definition. Component-specific primary results are not reported in the registry record.

The posted primary counts are 98 of 99 in the PTA-plus-MicroStent arm and 44 of 51 in the PTA-alone arm. The difference in observed proportions is expressed as a risk difference, with the PTA-alone group compared against PTA plus MicroStent. This gives an absolute comparison of the frequency of meeting the patency definition in the analyzed groups. It does not by itself describe time to loss of patency or establish why an outcome occurred. The registry does not report a time-to-event analysis for this endpoint.

7. Results Posted in the Registry

• Standard PTA: 86.3% (44/51) versus 99.0% (98/99) on control; risk difference -12.7 percentage points (95% CI -22.4 to -3.1), risk ratio 0.87 (0.78–0.97); 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.

Number of Subjects With Freedom From Major Amputation Above the Ankle

• 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:
  • Standard PTA: 98.0% (50/51) versus 99.0% (98/99) on control; risk difference -1.0 percentage points (95% CI -5.2 to 3.3), risk ratio 0.99 (0.95–1.03); unadjusted two-proportion z-test p = 0.631.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard PTA and the control. The interval gives the range of effects that remain compatible with the data.

Number of Subjects With Reduction in Size of Ischemic Leg/Foot Ulcers

• 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:
  • Standard PTA: 28.6% (4/14) versus 44.1% (15/34) on control; risk difference -15.5 percentage points (95% CI -44.5 to 13.4), risk ratio 0.65 (0.26–1.61); unadjusted two-proportion z-test p = 0.317.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard PTA and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies five secondary endpoints, including freedom from major amputation above the ankle, freedom from major adverse limb event, reduction in ischemic leg or foot ulcer size, and serious adverse events related to device or procedure. Arm-level numeric comparisons are posted for freedom from major amputation and reduction in ulcer size. Numeric results for the remaining listed secondary endpoints are not reported in the registry record in the same participant-count comparison format.

The secondary pattern is not a uniform reproduction of the primary result. The secondary estimates are less precise, and the reported intervals for the two posted comparisons include zero. Their unadjusted p-values do not provide clear evidence of a difference under the individual comparisons, but that does not demonstrate that the groups are equivalent or that a difference is absent. The secondary outcomes also address distinct clinical events, so they do not simply confirm or refute the primary patency measure.

These outcomes can help place the primary result in a broader context, but they carry less inferential weight when many outcomes are assessed without a reported multiplicity strategy. When multiple hypotheses are tested, the chance of at least one apparently unusual result can rise. The registry record does not report a hierarchy of testing, an adjustment, or a prespecified strategy controlling that issue. The secondary comparisons should therefore be treated as descriptive or exploratory evidence rather than as a collection of independent confirmatory conclusions.

The secondary endpoints also use different analyzed denominators. This affects precision and makes direct comparisons across outcomes inappropriate without understanding their definitions and populations. The registry record does not report the reasons for all denominator differences, detailed missing-data handling, or a complete set of outcome-specific analysis methods. The secondary results can inform questions for further evaluation, but they do not independently establish the interpretation of the primary endpoint.

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

• Number of Subjects With Freedom From Major Amputation Above the Ankle
• Number of Subjects With Freedom From Major Adverse Limb Event
• Number of Subjects With Reduction in Size of Ischemic Leg/Foot Ulcers
• Frequency and Severity of Serious Adverse Events Related to Device.
• Frequency and Severity of Serious Adverse Events Related to Procedure.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant is counted as having or not having target-lesion patency under the registry definition. For a binary outcome, a natural summary is the proportion meeting the endpoint in each arm. The posted comparison uses a risk difference: the proportion in the PTA-alone arm minus the proportion in the PTA-plus-MicroStent arm. This absolute measure expresses the difference in event proportions on the same scale as the underlying outcome. A negative value means the observed proportion was lower in the comparator arm under this ordering.

The posted primary comparison gives group proportions of 0.990 and 0.863 and a risk difference of -0.127. The interval from -0.224 to -0.031 expresses uncertainty about the estimated difference. A confidence interval is a range of estimates compatible with the data and the statistical procedure used; it is not a guarantee that the true value lies within the particular interval. The registry record does not specify the confidence-interval construction in the information reported with these results, so no additional assumptions about that calculation should be attached to it.

A p-value describes how unusual results at least as discrepant as those observed would be under a null model and the test’s assumptions. The primary unadjusted p-value is 0.001. It is not the probability that the null hypothesis is true, nor does it tell readers whether the magnitude is important in practice. It also does not account for testing multiple outcomes unless an adjustment is specified. A multiplicity adjustment is not reported in the registry record.

The risk difference is an unadjusted comparison from posted summary counts. An adjusted analysis could account for prespecified covariates or design factors, but no such model or adjusted result is reported in the registry record. The record also does not report the analysis method used by the sponsor, detailed handling of missing outcomes, or how participants were assigned to the analysis population beyond the mITT description. These omissions matter because different analysis choices can affect both the estimate and its uncertainty.

The posted secondary binary outcomes are also counts of participants meeting an event definition. For these outcomes, the denominators differ from the primary endpoint and from each other. In particular, the ulcer-reduction outcome uses smaller analyzed groups than the primary endpoint, and only participants included in those outcome counts contribute directly to those posted proportions. The record does not provide enough detail to determine why every denominator differs or how missing outcome information was handled.

For binary outcomes, the number of participants and the number meeting the endpoint jointly determine the observed proportion. Smaller denominators generally leave less information for estimating a proportion, especially when the outcome is uncommon or when the result is close to a boundary. This is why an interval should be read with its point estimate: the estimate describes the observed comparison, while the interval conveys how much uncertainty remains under the method used.

Over-dispersion is a general concern in some statistical models when observed variability exceeds what a model assumes. It is especially relevant for outcomes with grouped or repeated observations. The primary endpoint is posted as a participant-level binary count, and no over-dispersion model is reported. It would therefore be inappropriate to claim that an over-dispersion adjustment was used or needed for this posted comparison. More generally, model choice should match the structure of the outcome and the design; details of a model-based analysis are not reported in the registry record.

The sample-size planning figures are illustrations based on the observed effect and stated assumptions, not the trial’s original design calculation. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The effect used for each planning illustration is a stated fraction of the observed effect. These calculations answer a hypothetical planning question about the number of participants per arm that would be needed under those assumptions; they do not describe the trial’s actual enrollment target rationale. The original sample-size justification and its assumptions are not reported in the registry record.

Power is the probability, under a specified design and assumed effect, of detecting an effect using the stated statistical criterion. An 80% power column and a 90% power column show planning targets for different hypothetical studies, not a retrospective measure of the strength of this trial’s evidence. A higher target power generally requires more participants when other assumptions are held fixed. The planning figures also depend on the effect size assumed: planning for a smaller effect requires more participants. These are general statistical relationships; the registry does not report that the trial itself was designed using these particular calculations.

Finally, randomization and masking address different aspects of study design. Random assignment can support a fair comparison of groups, while masking can reduce some forms of influence on care, assessment, or reporting. The trial is reported as unmasked. Because the endpoint includes clinically driven reintervention, the open-label design is relevant to interpretation; the registry does not report whether endpoint assessment was independently adjudicated or whether any other safeguards were used.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.127, and its reported interval extends from -0.224 to -0.031. This interval communicates uncertainty about the absolute difference between the observed endpoint proportions. It is important to consider its width as well as its direction: the result points toward a lower observed patency proportion in the PTA-alone group, but the interval allows a range of possible differences rather than identifying a single exact effect.

The interval excludes zero, which is consistent with the unadjusted p-value of 0.001 for this comparison. This does not establish that the estimated magnitude is exact or that it has a particular clinical importance. Statistical evidence against a zero difference and precision about the size of a difference are related but distinct questions. The registry record does not state the interval’s construction method or report an adjusted interval.

The analyzed counts also matter for precision. The primary outcome uses 99 participants in the PTA-plus-MicroStent arm and 51 in the PTA-alone arm. The registry separately describes mITT counts of 117 and 59, and overall six-month analyzed counts of 99 and 55. It does not explain the difference between the 55-person description and the 51-person PTA denominator in the posted primary comparison. This limits assessment of how the analyzed sample relates to the stated population.

The secondary endpoint intervals are wider in some cases, reflecting less precision in those comparisons. In particular, the ulcer-reduction comparison has smaller denominators and an interval that spans values on both sides of zero. Such results should not be treated as precise evidence of either a difference or no difference. The amputation-freedom interval also spans zero. In general, an interval spanning zero means that the reported comparison is compatible with no difference under the stated interval method, as well as with values on either side. The registry does not report a formal equivalence or non-inferiority analysis.

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, not a record of the trial’s original design rationale. For these binary participant-count outcomes, the figures are participants per arm, rather than total events. The planning assumptions listed in the registry are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect.

The 80% power column indicates the planned number of participants per arm for a hypothetical study with an 80% chance of detecting the assumed effect under the specified assumptions. The 90% power column gives the corresponding planning target for a 90% chance. Higher target power generally requires a larger planned sample when the other assumptions are unchanged. Planning for a smaller effect also requires more participants because a smaller difference is harder to distinguish from random variation.

For example, the primary-outcome planning rows include scenarios based on 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The figures rise as the assumed effect is reduced, for both power targets. These values are conditional on the stated planning method and should not be read as recommendations independent of context. The registry record does not report the original sample-size justification, its assumed effect, or whether the trial’s own design used these assumptions.

This is not observed power. Observed power is not a useful substitute for reading the estimate and its uncertainty after results are available. The planning figures instead illustrate the scale of a future study that might be needed under the assumptions specified for each scenario. Any curve presenting these planning values is a visual expression of the same assumptions and should be read as planning information, not as evidence that the current trial had a particular probability of success.

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 = 0.990; treatment proportion p₁ = 0.863; average p̄ = 0.926.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3695 = 0.7241.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3584 = 0.3016.
4. n = (0.7241 + 0.3016)² / (-0.1272)² = 65.1, rounded up to 66 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 <- 0.98989898989899                          # control proportion
p1 <- 0.862745098039216                          # 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(3477604)
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 = 66 (80% power), 87 (90% power)
 75% of observed effect: n per arm = 93 (80% power), 124 (90% power)
 50% of observed effect: n per arm = 155 (80% power), 207 (90% power)
power.prop.test: 65.1 
Simulated power at n = 66 per arm: 0.880 (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 lists a primary endpoint and five secondary endpoints. It does not report how the endpoints were ordered for formal testing, whether a family of hypotheses was defined, or whether any multiplicity adjustment was applied. This matters because interpreting each p-value as if it were the only test can overstate the strength of evidence when several outcomes are examined. The primary unadjusted p-value should be read as an individual comparison, not as a result adjusted for all outcomes.

The record reports that the trial is randomized and provides mITT population counts, but a detailed analysis plan is not reported in the registry record. The definitions and implementation of the mITT population, handling of participants who did not contribute to a particular outcome, and treatment of missing outcome data are not fully described in the reported information. No imputation approach, sensitivity analysis, or missing-data assumption is reported. Differences between the population counts and posted outcome denominators are visible in the record, but their causes are not explained.

No formal analysis listings are reported. The registry therefore does not describe whether the primary comparison was prespecified in a statistical analysis plan, whether covariate adjustment was planned, or whether an interim analysis was conducted. These details should not be inferred from the posted counts. The registry record also does not report an independent adjudication process for endpoint events or explain whether decisions about clinically driven reintervention were reviewed by masked assessors.

These reporting gaps do not change the arithmetic of the posted comparisons, but they limit assessment of how the analyses were selected and carried out. A clear analysis plan, complete participant accounting, and transparent handling of multiple outcomes and missing observations would help readers judge the robustness of the estimates. In their absence, the results are best interpreted as the comparisons presented in the registry, with their reported uncertainty and limitations, rather than as a complete account of the trial’s statistical 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: vascular disorders (51.7%), cardiac disorders (23.3%), infections and infestations (20.0%), nervous system disorders (15.0%), musculoskeletal and connective tissue disorders (13.8%).

The adverse-event record lists serious adverse events affecting 86 of 116 participants in the MicroStent-plus-PTA group and 43 of 60 in the PTA-alone group. It also lists other adverse events affecting 74 of 116 and 31 of 60, respectively. These are participant counts, not event rates per unit of follow-up, and the record does not provide a comparative effect estimate or uncertainty interval for these safety counts. The denominators used for safety differ from the primary outcome denominators.

The record lists vascular disorders as the leading serious-event category at 51.7%, followed by cardiac disorders at 23.3%, infections and infestations at 20.0%, nervous system disorders at 15.0%, musculoskeletal and connective tissue disorders at 13.8%, and injury, poisoning and procedural complications at 12.9%. These categories and percentages describe the reported serious-event terms; they do not establish that an event was caused by a device or procedure.

The death fields list 86 for the MicroStent-plus-PTA group and 43 for the PTA-alone group. The registry record does not explain the context or denominator represented by these fields, so they should not be interpreted as a participant-level death comparison. Follow-up duration, event timing, severity breakdowns beyond the listed terms, and a comparative safety analysis are not reported in the information available.

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

The posted primary results show a higher observed proportion meeting the patency definition in the PTA-plus-MicroStent group than in the PTA-alone group among participants included in the six-month comparison. The risk difference is -0.127 when expressed as PTA alone minus PTA plus MicroStent, and its reported interval is -0.224 to -0.031. The unadjusted p-value is 0.001. These statistics describe the recorded endpoint comparison; they do not, by themselves, settle the broader interpretation of the trial.

The endpoint combines freedom from target-lesion occlusion with absence of clinically driven target-lesion reintervention and major amputation. The posted total does not reveal which component accounts for an outcome, whether events occurred early or later within follow-up, or whether the observed difference persists beyond the stated period. Component-specific results and time-to-event analyses are not reported in the registry record.

The primary comparison uses fewer participants than the stated mITT population. The record gives mITT counts of 117 and 59 and describes overall six-month analyzed counts of 99 and 55, while the posted primary denominators are 99 and 51. The reason for these differences is not reported. This is relevant when considering representativeness, missing outcomes, and how closely the posted comparison follows the randomized population.

Randomization is reported, but the registry does not provide enough detail to evaluate the allocation process or the full analysis strategy. The trial is unmasked, and a clinically driven reintervention is one component of the primary endpoint. The available record does not state whether event assessment was independently adjudicated or otherwise protected from knowledge of assignment. These features should inform how confidently the observed contrast is attributed to assigned treatment.

The result is not a guarantee of an individual participant’s outcome and is not a recommendation about care. It does not establish that one strategy is superior across all outcomes, nor does it establish absence of differences in secondary or safety outcomes. The secondary results have wider uncertainty and no reported multiplicity adjustment. The findings should be understood as the posted comparisons for the stated populations and timeframe, with the limitations of the registry reporting kept explicit.

17. Why This Trial Matters Statistically

STAND raises statistical questions that commonly arise in device trials: how to define a binary clinical endpoint, how to compare proportions between randomized groups, and how to interpret an estimate when the analysis denominator differs from the stated study population. Target-lesion patency is defined using several clinical and procedural components, so its count offers a compact summary but does not show the contribution of each component. That makes the endpoint definition central to understanding what the primary contrast represents.

The trial also illustrates why an effect estimate and its uncertainty should be read together. The observed risk difference gives an absolute comparison, while the interval conveys uncertainty about its size. The unadjusted p-value addresses a different question and does not replace the interval or establish the practical meaning of the result. Considering all three helps avoid treating a single statistic as a complete account of evidence.

Randomization is an important design feature, but interpretation also depends on transparent reporting of participant flow, analysis populations, missing outcomes, and endpoint assessment. Here, the record gives mITT and six-month population descriptions alongside outcome denominators that do not fully align, without explaining the differences. The unmasked design and clinically driven component of the primary endpoint make information about assessment procedures particularly relevant, but those details are not reported.

Finally, the secondary outcomes and sample-size illustrations show why multiplicity and planning assumptions matter. Secondary comparisons have their own denominators and uncertainty, while the planning figures depend on hypothetical effect sizes and stated assumptions rather than the original trial rationale. Distinguishing these planning calculations from evidence observed in the trial helps keep conclusions tied to what the registry record actually reports.

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.

Several limitations are specific to the available STAND record. The primary outcome population is described in more than one way: the mITT counts are 117 and 59, the six-month overall analyzed counts are 99 and 55, and the posted primary comparison uses 99 and 51. The registry record does not explain the difference between these figures. Without a participant-flow account or an explanation of outcome availability, readers cannot determine from the record why the analyzed denominators vary.

The trial is listed as unmasked. Because the primary definition includes clinically driven reintervention, knowledge of assignment could be relevant to decisions or assessment. The registry record does not report whether adjudication was independent, whether assessors were masked, or how clinical decisions were standardized. This does not establish bias, but it leaves an important design question unresolved.

The registry does not report a detailed statistical analysis plan, formal analysis listings, multiplicity procedures, missing-data methods, or the original sample-size justification. It also does not report an adjusted analysis or a time-to-event analysis for the primary endpoint. The posted comparisons therefore offer less information about robustness than a fully documented analysis would provide.

Safety counts use denominators that differ from those in the primary comparison, and the record does not provide a comparative safety estimate with an interval. The death fields are listed without enough context to interpret them as participant-level outcomes. For secondary outcomes, numeric comparisons are available for only some of the listed endpoints in the posted participant-count form, and the reported denominators vary. These gaps constrain comparisons across endpoints and limit conclusions beyond the reported figures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Clinical Evaluation of the MicroSTent® PeripherAl Vascular SteNt in Subjects With Arterial Disease Below the Knee (STAND) — NCT03477604.
• Registry record last updated 2026-10-08; status last verified 2026-07.
• Results first posted 2026-10-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

STAND is a randomized, multicenter, parallel-group, unmasked trial of PTA plus the MicroStent peripheral vascular stent system versus PTA alone for infrapopliteal lesions in people with peripheral arterial disease. The registry lists enrollment of 177, a phase of NA, and status as active, not recruiting. The primary endpoint is target-lesion patency up to 6 months after randomization.

The posted primary counts are 98 of 99 with patency in the MicroStent-plus-PTA arm and 44 of 51 in the PTA-alone arm. The risk difference, PTA alone minus MicroStent plus PTA, is -0.127, with an interval from -0.224 to -0.031 and an unadjusted p-value of 0.001. Secondary comparisons are less precise, and several details of population flow, missing-data handling, analysis planning, and safety interpretation are not reported in the registry record.