The PLATINUM Clinical Trial to Assess the PROMUS Element Stent System for Treatment of De Novo Coronary Artery Lesions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The PLATINUM Clinical Trial to Assess the PROMUS Element Stent System for Treatment of De Novo Coronary Artery Lesions (NCT00823212), a randomized phase 3 study. The primary outcome is Target Lesion Failure (TLF).

2. Clinical Question

3. Trial Design

NCT00823212, titled the PLATINUM clinical trial, was a phase 3, randomized, single-masked, parallel-group study sponsored by Boston Scientific Corporation. The registry lists enrollment of 1530 and a completed status. The start is recorded as 2009-01 and primary completion as 2010-09. These dates describe the registry record and do not, by themselves, provide details about recruitment duration, follow-up completion, or analysis timing.

Participants were assigned to receive either the PROMUS stent system or the PROMUS Element stent system. The registry describes the PROMUS group as receiving PROMUS (XIENCE V) and the PROMUS Element group as receiving PROMUS Element. The comparison was designed around treatment of up to two de novo atherosclerotic coronary artery lesions. The brief summary characterizes the principal lesion setting as average-length lesions in average-sized vessels. Companion sub-trials addressed smaller vessels and longer lesions, but their results are not reported in the registry record.

The primary endpoint was target lesion failure at 12 months after the index procedure. For its non-inferiority test, the registry identifies the per-protocol analysis set as the primary analysis population. It defines that set as all randomized participants who received their assigned treatment. Other analysis populations, including whether an intention-to-treat analysis was conducted, are not reported in the registry record.

The registry does not report the original sample-size justification, the planned non-inferiority margin, details of masking beyond the single-masked designation, or the allocation ratio. Those details should not be inferred from the observed group sizes or from the separate planning illustrations. The record lists 39 outcome measures and one analysis, while a set of secondary outcomes is also posted.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary analysis set for the non-inferiority testing of the primary endpoint, 12-month TLF, is the per-protocol analysis set. All randomized participants who received their assigned treatment are included in the per-protocol analysis set.

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 Target Lesion Failure (TLF), measured over 12-month post index procedure.

Target lesion failure (TLF) was the primary endpoint at 12-month post index procedure. It was defined as the occurrence of any of three events: ischemia-driven revascularization of the target lesion, myocardial infarction (Q-wave and non-Q-wave) related to the target vessel, or cardiac death related to the target vessel. The endpoint is reported as the percentage of participants with an event.

A composite endpoint combines several clinically relevant event types into one outcome. In general, this can capture more events than any single component and provide a summary of outcomes related to the treated lesion. However, the combined percentage does not show how much each component contributed. The registry’s definition does not assign different weights to its components, and the overall TLF result should not be read as if it were a result for each component separately.

The record specifies the per-protocol set for the primary non-inferiority analysis: randomized participants who received their assigned treatment. This population definition matters because the interpretation of a non-inferiority comparison can depend on which participants are included and how deviations or missing outcome information are handled. Details about missing data handling and the non-inferiority margin are not reported in the registry record.

TLF is used as the trial’s primary measure for comparing the stent groups at the stated follow-up. It summarizes revascularization, target-vessel-related myocardial infarction, and cardiac death, but does not establish that the groups are alike on every component or on outcomes beyond the measure and timeframe recorded.

7. Results Posted in the Registry

• PROMUS Element: 3.4% (25/731) versus 2.9% (21/714) on control; risk difference 0.5 percentage points (95% CI -1.3 to 2.3), risk ratio 1.16 (0.66–2.06); unadjusted two-proportion z-test p = 0.604.

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.

Target Lesion Failure (TLF)

• 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:
  • PROMUS Element: 0.9% (7/766) versus 1.4% (11/761) on control; risk difference -0.5 percentage points (95% CI -1.6 to 0.6), risk ratio 0.63 (0.25–1.62); unadjusted two-proportion z-test p = 0.336.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PROMUS Element and the control. The interval gives the range of effects that remain compatible with the data.

Target Vessel Failure (TVF)

• 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:
  • PROMUS Element: 0.9% (7/766) versus 1.4% (11/761) on control; risk difference -0.5 percentage points (95% CI -1.6 to 0.6), risk ratio 0.63 (0.25–1.62); unadjusted two-proportion z-test p = 0.336.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PROMUS Element and the control. The interval gives the range of effects that remain compatible with the data.

Myocardial Infarction (MI) Related to the Target Vessel

• 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:
  • PROMUS Element: 0.7% (5/766) versus 1.3% (10/761) on control; risk difference -0.7 percentage points (95% CI -1.7 to 0.3), risk ratio 0.50 (0.17–1.45); unadjusted two-proportion z-test p = 0.190.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PROMUS Element and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover TLF, target vessel failure, and myocardial infarction related to the target vessel at 30 days. Across these outcomes, the event percentages are low, and the recalculated comparisons are imprecise. The TLF and TVF summaries have the same posted arm percentages and recalculated comparison statistics. The myocardial infarction comparison points in the same direction as the 30-day TLF and TVF comparisons, but these observations remain secondary and should not be treated as separate replications of the primary result.

In relation to the primary endpoint, the secondary outcomes provide short-term descriptions of related events, whereas the primary TLF endpoint is assessed at 12 months and combines several event types. Differences in follow-up and endpoint definition mean the secondary findings do not directly confirm or overturn the primary analysis. The registry lists 38 posted secondary outcomes, while only a subset is described in the outcome information available for this analysis.

The recalculated secondary comparisons are unadjusted. When many outcomes are examined, the chance of finding apparently notable results by chance increases unless the analysis accounts for multiplicity or clearly treats the results as exploratory. No multiplicity adjustment or prespecified hierarchy for the secondary endpoints is reported in the registry record. The secondary p-values therefore carry less weight than the prespecified primary analysis and should be interpreted cautiously.

These data can describe the pattern across the posted secondary outcomes, but they do not establish a treatment effect for every endpoint or show that all outcomes have been considered. The missing multiplicity details, incomplete reporting of the broader outcome set, and limited precision of rare-event comparisons all constrain the strength of conclusions that can be drawn from secondary analyses.

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

• Target Lesion Failure (TLF)
• Target Lesion Failure (TLF)
• Target Lesion Failure (TLF)
• Target Vessel Failure (TVF)
• Target Vessel Failure (TVF)
• Target Vessel Failure (TVF)
• Myocardial Infarction (MI) Related to the Target Vessel
• Myocardial Infarction (MI) Related to the Target Vessel

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a randomized, parallel-group comparison and identifies the primary endpoint as a percentage of participants with TLF. For a binary outcome, each participant is classified as having or not having the event during the specified follow-up. Group percentages summarize the observed event frequency, while comparative measures estimate how the groups differ. The registry’s arm-level percentages and the recalculated contrast therefore answer related but not identical descriptive questions.

What does the risk difference represent?

The risk difference expresses the event probability in one group minus the event probability in the comparison group. In the recalculation, PROMUS is the reference and PROMUS Element is the comparison. A risk difference of zero corresponds to equal estimated event probabilities. A positive estimate means the event percentage is higher in the comparison group; a negative estimate means it is lower. The reported recalculated estimate is 0.005, and its confidence interval is -0.013 to 0.023. Those are proportions, not percentage-point values. No conversion is needed to interpret the direction or whether the interval includes zero.

General statistical explanation: the risk difference is an absolute measure. It can be useful for understanding how far apart two event probabilities are on the probability scale. It differs from a risk ratio, which compares probabilities as a ratio, and from an odds ratio, which compares event odds. Relative measures can convey a different impression from absolute differences, particularly when outcomes are uncommon. Neither type of measure removes uncertainty from the data.

What does the confidence interval tell us?

A confidence interval describes the range of values reasonably compatible with the data under the calculation’s statistical assumptions. It is not a guarantee that the true effect lies inside that particular interval, and it does not mean that every value in the interval is equally likely. Here, the recalculated interval for the risk difference extends from a negative to a positive value, including zero. That means the unadjusted data are compatible with no difference as well as with differences in either direction over the interval’s range. It does not prove equality.

The risk ratio is reported as 1.163, with limits 0.657 and 2.058. The odds ratio is reported as 1.169, with limits 0.648 and 2.107. For ratios, the null value is one; both reported intervals include it. These intervals are also wide enough to indicate substantial uncertainty about the relative effect. The measures describe the same event data using different scales, so they should not be interpreted as separate independent trials.

How is a non-inferiority test different?

In a conventional difference test, the central question is whether the observed data provide evidence against no difference. A non-inferiority test asks whether the treatment being evaluated is not worse than the comparator by more than a prespecified amount. That amount is the non-inferiority margin. General statistical explanation: a non-inferiority conclusion depends on the estimate and its confidence bound relative to that margin, not simply on whether a difference-test p-value is above or below a conventional threshold.

The registry reports a Farrington-Manning test for the primary comparison and classifies it as non-inferiority/equivalence. It reports a value of 0.5, an upper confidence limit of 2.13, a 95% confidence level, and p = 0.001. The margin is not reported in the registry record, and the lower confidence limit is also absent. Thus, the reported result can be described, but its decision threshold cannot be independently checked from the posted information. The unadjusted recalculation is not the sponsor’s formal test and should not be used to replace it.

Why can the recalculation differ?

The recalculated statistics are simple unadjusted comparisons based on the posted summary statistics. The formal analysis may use a specified test and analysis framework rather than the same calculation. The registry record does not provide enough detail to identify all reasons for the difference. It would be inappropriate to infer a particular adjustment, data-handling rule, or analytic choice that is not reported. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence when describing the formal analysis.

General statistical explanation: when the target is rare, changing a small number of event classifications can have a noticeable effect on a percentage or contrast. Different methods can also yield different uncertainty estimates or test results, especially when an analysis tests a one-sided non-inferiority hypothesis rather than a two-sided difference hypothesis. The methods and hypotheses need to be kept distinct when reading their outputs.

Why does over-dispersion matter?

Over-dispersion is a general issue in outcomes modeled as counts or rates: it occurs when variation exceeds what a particular statistical model assumes. In such settings, an analysis that ignores the extra variation may understate uncertainty. The primary outcome is reported as a binary percentage, and the registry does not report an over-dispersion model or a count-based primary analysis. Over-dispersion therefore should not be invoked as an explanation for the reported discrepancy. For any specific model-based analysis, its assumptions would need to be documented before drawing conclusions about whether over-dispersion was relevant.

11. Confidence Intervals and Precision

The arm percentages for the 12-month primary endpoint are 2.9% for PROMUS and 3.4% for PROMUS Element. These percentages are close descriptively, but closeness of point estimates is not the same as precision. Precision is better assessed by the range of estimates compatible with the data, as represented by a confidence interval, and by the analysis framework appropriate to the question.

The recalculated risk difference is 0.005, with a 95% confidence interval from -0.013 to 0.023. The span includes zero and values in both directions. It therefore does not narrow the possible difference to a single direction. The ratio estimates have intervals that also include their null value of one: 0.657 to 2.058 for the risk ratio and 0.648 to 2.107 for the odds ratio. These intervals indicate uncertainty in the magnitude of the relative contrast as well as its direction.

General statistical explanation: a confidence interval is more informative than a point estimate alone because it conveys sampling uncertainty under the method used. A wide interval means the observed data are consistent with a broader range of effects; a narrow interval would indicate greater precision. The interval does not account automatically for every source of uncertainty, such as missing outcomes, design limitations, or the consequences of testing multiple endpoints.

The sponsor’s reported non-inferiority analysis gives a 95% upper confidence limit of 2.13 but does not report the lower limit. Since the non-inferiority margin is not reported in the registry record, the upper limit cannot be compared with the decision threshold from the available information. The sponsor’s formal analysis remains the relevant analysis for its stated non-inferiority question, while the recalculated interval is an unadjusted illustration. Neither interval should be read as establishing that the groups are identical.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculation. For these binary outcomes, the figures are participants per arm. 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 the stated fraction of the observed effect. In general, time-to-event planning figures use total events, but the outcomes are not time-to-event outcomes.

The 80% power column describes the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning quantity for a higher chance of detection. Power is a design property under a chosen model and effect size; it is not a measure of how likely the observed result is to be true.

The rows represent planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect requires more participants to distinguish it from random variation with the stated power and significance level. For example, the planning figures rise as the assumed fraction of the observed effect decreases. This pattern is a general feature of sample-size planning, not evidence that such a difference exists or will occur in a future study.

These calculations are not observed power. They do not describe the power actually achieved by the completed trial, and they do not revise the original trial design. The original sample-size assumptions and justification are not reported in the registry record. The planning illustrations should therefore be read as conditional examples based on their stated assumptions, not as an explanation of why enrollment was chosen or as a recommendation for a new study.

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 = 0.029; treatment proportion p₁ = 0.034; average p̄ = 0.032.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2482 = 0.4864.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2481 = 0.2088.
4. n = (0.4864 + 0.2088)² / (0.0048)² = 21,085.3, rounded up to 21,086 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 <- 0.0294117647058824                          # control proportion
p1 <- 0.0341997264021888                          # 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(823212)
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 = 21,086 (80% power), 28,227 (90% power)
 75% of observed effect: n per arm = 36,804 (80% power), 49,269 (90% power)
 50% of observed effect: n per arm = 81,271 (80% power), 108,799 (90% power)
power.prop.test: 21085.3 
Simulated power at n = 21,086 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Farrington-Manning test for non-inferiority/equivalence. Its reported difference in percent of participants is 0.5, the 95% upper confidence limit is 2.13, and p = 0.001. The lower confidence limit is not reported in the registry record. The registry does not state the non-inferiority margin, so the reported upper limit cannot be compared with that threshold using the posted information alone.

The recalculated comparison is a simple unadjusted contrast from the posted summary statistics. It gives a risk difference of 0.005, a 95% confidence interval from -0.013 to 0.023, and an unadjusted p-value of 0.604. These values do not reproduce the sponsor’s reported analysis. The registry flags a discrepancy, and the sponsor’s own analysis takes precedence for describing the formal non-inferiority result.

The two outputs address related but not interchangeable analyses. The recalculation is an unadjusted comparison of the posted event summaries; the reported Farrington-Manning result is the sponsor’s stated non-inferiority analysis. The record does not provide enough information to determine precisely why their estimates or p-values differ, so a specific explanation should not be assumed. The recalculated result can help readers see the raw comparative scale and uncertainty, but it cannot replace the sponsor’s formal test or establish the trial’s non-inferiority conclusion independently.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint and the posted secondary endpoints pose different interpretation questions. The registry identifies 12-month TLF as the primary endpoint and lists 38 secondary outcomes, but it does not report a multiplicity plan, a testing hierarchy, or an adjustment procedure for the secondary comparisons. Without such details, secondary p-values should not be treated as if each were an isolated confirmatory test. General statistical explanation: examining many outcomes can increase the chance of at least one apparently unusual result arising by chance; multiplicity procedures aim to manage that risk, often at the cost of making individual tests more conservative.

The record specifies that the primary non-inferiority analysis used the per-protocol set, defined as all randomized participants who received their assigned treatment. It does not report whether an intention-to-treat or modified intention-to-treat analysis was also conducted, nor does it explain how protocol deviations were handled beyond the stated population definition. This matters because non-inferiority conclusions can be sensitive to analysis population and adherence patterns.

Missing-data methods are not reported in the registry record. The record does not state how missing 12-month outcomes were handled, whether participants lost to follow-up differed between groups, or whether sensitivity analyses were performed. Those details are important for judging whether the observed percentages could be affected by incomplete follow-up. No assumptions about the direction or magnitude of any missing-data effect should be made without those details.

Interim analyses and stopping rules are not reported in the registry record. The original sample-size justification, the non-inferiority margin, and the full statistical analysis plan are also not reported. Consequently, readers cannot verify the planned decision threshold, assess any planned adjustment for interim looks, or determine whether the posted analyses cover all prespecified outcomes. These omissions limit independent appraisal of the formal testing framework, even though the registry does identify the primary endpoint, analysis population, and named test.

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: angina pectoris (5.7%), non-cardiac chest pain (4.2%), angina unstable (2.0%), coronary artery dissection (1.8%), chest pain (1.0%).

The adverse-event record lists serious adverse events for both groups, with 762 at risk and 237 affected in PROMUS, and 768 at risk and 238 affected in PROMUS Element. For other adverse events, it lists 762 at risk and 190 affected in PROMUS, and 768 at risk and 197 affected in PROMUS Element. These are the posted counts; no additional percentages have been calculated. The field for deaths has no value, so deaths are not reported in the registry record.

The most frequent listed serious terms include angina pectoris at 5.7%, non-cardiac chest pain at 4.2%, unstable angina at 2.0%, coronary artery dissection at 1.8%, chest pain at 1.0%, and chronic obstructive pulmonary disease at 0.9%. The registry lists these terms and percentages; it does not provide enough detail to determine overlap between categories, timing, attribution, or whether each event occurred in a participant with more than one event.

Serious adverse-event figures are safety summaries, not the primary efficacy comparison. Differences in affected counts should be interpreted in light of the numbers at risk, event definitions, follow-up, and any missing safety data. Those additional details are not reported in the registry record, so the posted figures should not be extended into broader conclusions about comparative safety.

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

The registry record describes a randomized comparison of two everolimus-eluting coronary stent systems in patients with de novo coronary artery lesions. The primary outcome was TLF at 12 months. The posted percentages are 2.9% for PROMUS and 3.4% for PROMUS Element. The sponsor’s analysis is labeled as a non-inferiority/equivalence analysis, while the simple recalculation gives an unadjusted estimate and interval that differ from that reported analysis.

These results do not establish that the two stent groups are identical. A non-significant result in a conventional difference test is not proof of equality, and a non-inferiority conclusion depends on the margin and analysis framework. The margin is not reported in the registry record. The sponsor’s own analysis takes precedence over the recalculation for the formal non-inferiority question, but the missing margin and lower confidence limit prevent independent evaluation of the stated decision threshold from the registry information alone.

The primary endpoint is a composite. Its overall result does not show the separate contribution of revascularization, myocardial infarction, and cardiac death. Nor does it establish results for outcomes beyond the listed definitions and follow-up period. The secondary outcome summaries are shorter-term and unadjusted, so they provide descriptive context rather than independent confirmation of the primary result.

General statistical explanation: a study result is an estimate with uncertainty, not a guarantee that the same event percentages would be observed in another population or setting. The confidence intervals for the recalculated comparisons span the null values, reflecting uncertainty about the direction and size of the contrasts. The registry record does not report the details needed to evaluate missing outcomes, multiplicity handling, or the complete prespecified analysis plan.

Accordingly, the posted findings support a bounded description of the trial’s reported outcomes and analyses. They do not justify claims about every possible clinical outcome, all lesion types, longer-term results, or populations beyond those represented by the study. Medical decisions require context beyond these statistical summaries and are not addressed by this interpretation.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical question must be matched to the analysis. A conventional difference comparison and a non-inferiority test are not interchangeable. The recalculated risk difference describes an unadjusted contrast, while the registry’s sponsor-reported Farrington-Manning test addresses non-inferiority/equivalence. The discrepancy means both outputs need to be identified clearly, with the sponsor’s own analysis taking precedence for the formal test.

The case also shows why a non-inferiority margin is essential for interpretation. A test result and confidence bound cannot be judged against a clinical decision threshold unless that threshold is known. The registry record reports the analysis type and part of its result, but not the margin or the lower confidence limit. This leaves a gap between knowing what test was reported and independently evaluating its decision rule.

Rare binary outcomes can produce deceptively simple percentages alongside substantial uncertainty. The primary event percentages are close, yet the recalculated confidence interval spans values on both sides of no difference. General statistical explanation: the number of observed events, not only the total number enrolled, contributes to the precision of an estimate. This is why estimates for uncommon outcomes can remain uncertain even in a sizable randomized study.

Finally, the record highlights the importance of population definitions, missing-data methods, and multiplicity plans. The primary analysis population is identified, but handling of missing outcomes and the approach to the many secondary measures are not reported. Clear reporting of these choices is necessary for readers to distinguish a confirmatory finding from descriptive or exploratory patterns.

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.

Several trial-specific reporting gaps limit interpretation. The non-inferiority margin is not reported in the registry record, and the reported sponsor analysis does not include a lower confidence limit. The registry identifies the analysis as non-inferiority/equivalence, but the available information does not allow independent comparison of its upper confidence limit with the planned decision threshold.

The registry flags a discrepancy between the sponsor’s analysis and the unadjusted recalculation. The sponsor’s own analysis takes precedence, but the record does not provide enough information to explain why the results differ. The recalculation therefore serves only as a simple comparison of posted summaries and should not be treated as a replacement for the trial’s formal analysis.

The primary analysis uses a per-protocol population defined as randomized participants who received assigned treatment. Details about other analysis populations, protocol deviations, missing outcome data, and sensitivity analyses are not reported in the registry record. These details are relevant to non-inferiority interpretation. The registry also does not report the original sample-size justification, interim analyses, or a full multiplicity plan.

The primary endpoint is composite, so the overall TLF result does not show the separate results for each component. The posted secondary outcomes are unadjusted, and the record does not give a full analysis hierarchy. Companion sub-trials for smaller vessels and longer lesions are described, but their results are not reported in the registry record. The record’s brief description of average-length lesions in average-sized vessels also limits how far results should be extended to other lesion settings.

Safety summaries list counts and selected serious-event terms, but deaths are not reported in the registry record, and further details about timing, attribution, overlap, and missing safety follow-up are not provided. These reporting limitations do not determine the direction of any unreported result; they mark what cannot be assessed from the registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The PLATINUM Clinical Trial to Assess the PROMUS Element Stent System for Treatment of De Novo Coronary Artery Lesions — NCT00823212.
• Registry record last updated 2019-03-27; status last verified 2019-03.
• Results first posted 2012-01-27.
• 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

NCT00823212 is a completed phase 3 randomized, single-masked, parallel-group trial comparing PROMUS with PROMUS Element for treatment of up to two de novo coronary artery lesions. The registry lists enrollment of 1530 and identifies 12-month TLF as the primary endpoint, analyzed in a per-protocol population.

The posted primary percentages are 2.9% for PROMUS and 3.4% for PROMUS Element. The sponsor’s reported Farrington-Manning non-inferiority/equivalence analysis gives a value of 0.5, an upper 95% confidence limit of 2.13, and p = 0.001; the non-inferiority margin is not reported in the registry record. The unadjusted recalculation differs, so the sponsor’s own analysis takes precedence for the formal test.

Interpretation is limited by the missing margin, incomplete analysis details, unreported missing-data and multiplicity methods, and the discrepancy between analyses. Secondary and safety summaries provide additional descriptive information but do not remove those limitations.