Superficial Vein Thrombosis (SVT) Treated With Rivaroxaban Versus Fondaparinux: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Superficial Vein Thrombosis (SVT) Treated With Rivaroxaban Versus Fondaparinux (NCT01499953), a randomized phase 3 study. The primary outcome is Rate of Objectively Confirmed VTE Complications.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, open-label, parallel-group trial comparing rivaroxaban with fondaparinux for SVT. The registry lists enrollment of 472 and identifies GWT-TUD GmbH as the sponsor. The record gives a start of 2012-04, primary completion of 2016-05, and status of completed. Those details describe the registered study; they do not by themselves establish how many participants contributed to each particular endpoint.

The treatment descriptions specify 45 days of therapy in both groups. Rivaroxaban was given orally at 10 mg OD, while fondaparinux was given subcutaneously at 2,5 mg OD. Because masking was listed as none, the design was open-label rather than blinded. The registry record does not explain the randomization sequence, allocation concealment, treatment adherence, or the handling of treatment discontinuation.

The primary outcome was a participant count for a composite efficacy endpoint, assessed in the per protocol set at 45 +/- 5 days. The posted group counts are 7.0 among 211.0 for rivaroxaban and 4.0 among 224.0 for fondaparinux. These endpoint-specific denominators differ from the safety denominators reported elsewhere in the record; they should not be silently substituted for one another.

The record names secondary outcomes, including a composite efficacy outcome, major VTE, and surgery for SVT. Some secondary results are posted at 90 +/- 10 days or 90 +/-10 days, while a result for major VTE is not reported in the registry record. The registry record does not provide the full protocol, the original sample-size justification, or the planned analysis details beyond the reported non-inferiority test.

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: 472 patients were randomized to one of the two treatment groups. One patient in the fondaparinux group withdrew consent after randomization but before the first study drug administration.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Per protocol 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.

Population: Safety analysis set (Per protocol analysis set for risk factors)

6. Primary Endpoint

The registry lists the primary outcome as Rate of Objectively Confirmed VTE Complications, measured over 45 +/- 5 days.

The primary endpoint was the rate of objectively confirmed VTE complications, measured as the number of participants with an event. It was a composite: death from any cause; symptomatic pulmonary embolism confirmed by specified imaging or autopsy; symptomatic deep vein thrombosis confirmed by ultrasonography or venography; or symptomatic extension towards the saphenofemoral junction or symptomatic recurrence of SVT confirmed by ultrasonography. Events were counted up to day 45, with the listed timeframe of 45 +/- 5 days.

A composite can capture several clinically relevant event types in one outcome. In general, combining outcomes can make an endpoint more informative when the separate events are related to the trial question, but it also means the overall result does not show which component chiefly contributed. The posted primary result is a participant count for the composite, not a separate estimate for every component. Component-specific primary results are not reported in the registry record.

Objective confirmation requirements help define which events qualify, rather than relying only on an unverified report of symptoms. The endpoint is therefore a defined measure of events documented by the specified procedures. It does not, by itself, describe symptom burden or other outcomes outside the composite. The per protocol population is specified for this endpoint; further detail on how that population was constructed is not reported in the registry record.

7. Results Posted in the Registry

• Fondaparinux: 1.8% (4/224) versus 3.3% (7/211) on control; risk difference -1.5 percentage points (95% CI -4.5 to 1.4), risk ratio 0.54 (0.16–1.81); unadjusted two-proportion z-test p = 0.309.

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.

Composite Primary Efficacy Outcome

• 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:
  • Fondaparinux: 6.7% (15/224) versus 7.1% (15/211) on control; risk difference -0.4 percentage points (95% CI -5.2 to 4.4), risk ratio 0.94 (0.47–1.88); unadjusted two-proportion z-test p = 0.865.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fondaparinux and the control. The interval gives the range of effects that remain compatible with the data.

Rates of Surgery for SVT

• 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:
  • Fondaparinux: 0.9% (2/224) versus 0.0% (0/211) on control; risk difference 0.9 percentage points (95% CI -0.3 to 2.1); unadjusted two-proportion z-test p = 0.169.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fondaparinux and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results offer a limited additional view of outcomes beyond the primary endpoint. The composite primary efficacy outcome is reported at 90 +/- 10 days, and surgery for SVT is reported at 90 +/-10 days. The registry also names rate of major VTE as a secondary outcome, but its result is not reported in the registry record. The tables should be read as separate endpoint summaries, not as a pooled or overall treatment effect.

At a broad level, the secondary results do not remove the uncertainty seen in the primary comparison. Their event counts are sparse, and a lack of a clear difference in a secondary comparison would not establish that the groups are equivalent. Secondary endpoints may add context, but they do not replace the primary endpoint or supply the missing details of the sponsor’s non-inferiority analysis. The posted secondary outcomes also use a later timeframe than the primary endpoint, so they concern a different follow-up window.

In general, when several endpoints are examined, the chance of seeing apparently notable results across the collection can increase, especially if interpretation focuses on individual unadjusted comparisons. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Accordingly, these secondary comparisons should be treated as exploratory context rather than independent confirmatory evidence. Their p-values and estimates should not be given the same weight as a prespecified primary analysis, particularly when the full analysis plan and multiplicity strategy are unavailable.

The overall pattern is therefore best described cautiously: secondary outcomes add some follow-up information, but the posted set is incomplete and does not resolve the primary result’s imprecision. The endpoint-specific rows and plots contain the individual counts and comparisons; repeating them as a single summary would obscure that each outcome represents a distinct measure and timeframe.

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

• Composite Primary Efficacy Outcome
• Rate of Major VTE
• Rates of Surgery for SVT

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

In general, a risk difference compares the proportions of participants with an event in two groups by subtracting one group’s proportion from the other’s. Its sign depends on the order of the groups. Here the posted comparison is fondaparinux relative to rivaroxaban, and the estimated risk difference is -0.015. The associated interval runs from -0.045 to 0.014. Because it spans the no-difference value, the estimate is compatible with effects in either direction. The interval is more informative about uncertainty than the point estimate alone.

How do relative measures differ?

In general, a risk ratio compares event proportions as a ratio, while an odds ratio compares event odds. They use different scales from the risk difference and can be less directly interpretable as absolute changes. The posted risk ratio is 0.538, with interval limits of 0.160 and 1.812. The posted odds ratio is 0.530, with interval limits of 0.153 and 1.837. The intervals cover values below and above the no-association value, so these relative estimates also leave substantial uncertainty. All of these measures are based on the same primary endpoint counts; they are not independent confirmations.

What does the unadjusted p-value test?

In general, an unadjusted p-value summarizes how unusual results at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The recalculated unadjusted p-value is 0.309. It pertains to the simple group comparison derived from posted summary statistics, not the sponsor’s non-inferiority test. The registry record does not state that the recalculation was the trial’s prespecified primary analysis.

What is different about a non-inferiority test?

In general, a non-inferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified margin. That is not the same question as whether there is any difference between groups. The margin determines what amount of difference is considered acceptable for the test, and the analysis plan determines how the evidence is evaluated. The registry reports an asymptotic test for non-inferiority with p = 0.025, but the margin, confidence interval for that test, and further decision criteria are not reported in the registry record. It is therefore not possible to reconstruct the sponsor’s test from the posted counts alone.

The asymptotic description indicates that the sponsor’s reported test used an approximation rather than a method based on an exact small-sample distribution. In general, approximation-based tests rely on their assumptions to represent the sampling behavior of the statistic. The registry record does not provide enough methodological detail to evaluate those assumptions or reproduce the sponsor’s analysis.

Why does the analysis population matter?

The primary endpoint is reported for the per protocol set. In general, a per protocol analysis focuses on participants meeting protocol-related requirements, while an analysis including all randomized participants addresses a different estimand and can be affected differently by departures from assigned treatment. The record does not report the full population definition, exclusions, or a parallel intention-to-treat result. It also does not explain how missing outcome data were handled. Those omissions limit assessment of how population selection and missingness could affect the result.

Since the trial was open-label, participants and study personnel were not masked according to the registry entry. The primary outcome includes objectively confirmed events, which gives the endpoint defined confirmation requirements. Still, the registry record does not describe blinded outcome adjudication or other procedures intended to reduce assessment bias. No such procedures should be assumed.

The reported comparisons are based on event counts, and the registry describes the primary outcome unit as participants. In general, when events are uncommon, a small change in the number of observed events can have a noticeable effect on estimated proportions and can leave intervals wide. That helps explain why a point estimate alone should not be treated as a precise answer. The posted counts and intervals should be read together, with the sponsor’s formal non-inferiority analysis kept distinct from recalculations made from summary data.

11. Confidence Intervals and Precision

The risk-difference interval for the primary comparison extends from -0.045 to 0.014 around the estimate of -0.015. It includes the no-difference value and allows for effects in either direction. Its width means the posted counts do not support a narrowly specified estimate of the group difference. The relative-effect intervals are also broad: 0.160 to 1.812 for the risk ratio and 0.153 to 1.837 for the odds ratio. They likewise span their no-association values.

In general, an interval is a range of estimates compatible with the data and the method used, under the method’s assumptions. It is not a guarantee that the true effect lies within the interval, nor does it express the probability that a particular effect is true. The registry does not state the confidence level for these recalculated intervals, so a confidence percentage should not be inferred from this record.

The limited primary event counts are relevant to precision: the posted groups have 7.0 and 4.0 participants with events. With relatively few events, the data provide limited information about the range of plausible effects. The interval is consequently important context for the point estimate and the p-value. A p-value alone cannot convey this range.

The sponsor’s non-inferiority result should not be assigned the recalculated interval or interpreted as if it tested the same hypothesis. The registry provides a p-value for the sponsor’s asymptotic non-inferiority analysis but does not report its interval or margin. That missing information prevents a direct account of the sponsor analysis’s precision against its decision threshold.

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 table and curve are planning illustrations based on the observed effect, not the trial’s original design calculation. For these non-time-to-event outcomes, the figures are participants per arm, not total events. 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 to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under those assumptions for a design with 80% power to detect the specified effect. The 90% power column gives the corresponding per-arm planning figure for a design with 90% power. These are prospective planning quantities, not a description of what the completed trial was powered to establish. This is not observed power.

The rows show planning for 100%, 75%, and 50% of the observed effect. For the primary endpoint, The table shows 1,663 participants per arm for 80% power and 2,225 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the figures are 3,172 and 4,246; for 50%, they are 7,622 and 10,203. The illustration therefore makes clear that smaller effects need more participants to detect under the stated assumptions. The curve visualizes the same planning relationship; it is not evidence about the results of this trial or a substitute for an original protocol-based calculation.

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 = 0.033; treatment proportion p₁ = 0.018; average p̄ = 0.026.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2230 = 0.4371.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2227 = 0.1875.
4. n = (0.4371 + 0.1875)² / (-0.0153)² = 1,662.3, rounded up to 1,663 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 <- 0.033175355450237                          # control proportion
p1 <- 0.0178571428571429                          # 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(1499953)
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 = 1,663 (80% power), 2,225 (90% power)
 75% of observed effect: n per arm = 3,172 (80% power), 4,246 (90% power)
 50% of observed effect: n per arm = 7,622 (80% power), 10,203 (90% power)
power.prop.test: 1662.3 
Simulated power at n = 1,663 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 posted result is identified as an asymptotic test for non-inferiority, with p = 0.025. The recalculated result is an unadjusted comparison of the posted primary event counts, with risk difference -0.015, interval -0.045 to 0.014, and p-value 0.309. These analyses do not answer precisely the same statistical question: a non-inferiority test evaluates a prespecified margin, while the unadjusted recalculation compares groups without that margin.

The record does not report the sponsor’s non-inferiority margin, its interval estimate, or enough details to reproduce its test. The differing results should therefore not be treated as a simple contradiction between two tests of an identical hypothesis. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence when describing the trial’s reported formal analysis. The recalculation is useful as a transparent, simple comparison from the posted summary statistics, but it does not replace the sponsor’s analysis.

Without the margin and fuller analysis details, the sponsor’s p-value cannot be translated into an independent judgment about whether the non-inferiority criterion was met. Nor should the recalculated p-value be used to overturn the sponsor’s reported analysis. The appropriate account is to present the two methods distinctly and acknowledge what is missing from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes, including the primary composite and secondary measures. When investigators examine more than one endpoint, multiple tests can create more opportunities for chance findings. In general, a prespecified hierarchy, family-wise error procedure, or other multiplicity strategy can clarify how evidence across endpoints is to be interpreted. The registry record does not report a multiplicity adjustment, an endpoint hierarchy, or the full statistical analysis plan. It is therefore not possible to determine from this record how the sponsor intended to control or interpret multiplicity.

This matters especially for secondary results. Unadjusted secondary p-values do not account for the number of outcomes examined. They can describe the individual posted comparisons, but should not be treated as if they were protected confirmatory tests. The record names rate of major VTE as a secondary outcome, but a result is not reported in the registry record. The extent of the full planned outcome set and any additional analyses is also not clear from the posted details.

For the primary endpoint, the population is identified as the per protocol set. The record does not provide a detailed definition of that set, a participant flow account, or a corresponding result for another analysis population. It does not report how missing outcome data were handled, whether any observations were excluded after randomization, or whether sensitivity analyses were performed. These details matter because population selection and missing data can influence an estimate, particularly when event counts are limited.

The registry also does not report interim analyses, stopping rules, or the original sample-size justification. These elements should not be inferred from the completed status or the planning illustration displayed with the results. Overall, the absence of these details limits assessment of prespecification, robustness, and the relationship between the reported analysis and the original trial plan.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: diabetic foot syndrome with tissue infection (0.4%), hospitalisation for copd exacerbation (0.4%), transient ischemic attack (0.4%), sigmoid diverticulitis (0.4%), suspected infection-associated seizure (0.4%).

The safety summary reports serious adverse events for groups with 235 participants at risk in the fondaparinux group and 236 in the rivaroxaban group. Serious events affected 3 participants in the fondaparinux group and 7 in the rivaroxaban group. Other adverse events affected 0 participants in each group. Deaths were reported for 0 participants receiving fondaparinux and 1 receiving rivaroxaban. These are the safety counts as posted; the denominators are not the primary efficacy denominators.

The registry lists serious-event terms including diabetic foot syndrome with tissue infection, hospitalisation for COPD exacerbation, transient ischemic attack, sigmoid diverticulitis, suspected infection-associated seizure, and lung cancer, each shown as 0.4%. These terms describe events recorded in the safety data, not evidence that a study treatment caused them. The registry summary does not provide enough detail to assess event timing, relatedness judgments, or the full clinical context.

In general, safety counts are descriptive and should be interpreted with their group sizes, follow-up, event definitions, and attribution procedures in mind. Those further details are not reported in the registry record. The counts alone do not establish a comparative safety conclusion.

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

The posted data describe a randomized comparison of two treatments and a primary composite of objectively confirmed events assessed up to day 45. The observed primary counts were 7.0 participants among 211.0 for rivaroxaban and 4.0 among 224.0 for fondaparinux. The recalculated interval spans the no-difference value, and the relative-effect intervals span their no-association values. This means the summary data leave substantial uncertainty about the size and direction of the primary comparison.

The sponsor’s own reported analysis was a non-inferiority test, not the same unadjusted test used for the recalculation. Its p-value is 0.025, but the registry record does not report the margin needed to independently interpret the test. The sponsor’s analysis takes precedence over the recalculation as the trial’s formal reported analysis, while the missing margin limits what can be concluded from the registry entry alone.

The results do not demonstrate that the treatments are identical, and they do not establish that one is superior. A result that does not show a clear difference is not proof of equivalence. Similarly, a non-inferiority p-value without its margin and analysis context is not enough to independently assess the non-inferiority claim. The evidence should be described with these distinctions intact.

The findings apply to the recorded endpoint, analysis population, and follow-up periods. The primary analysis is specified for the per protocol set; the record does not provide full eligibility details, missing-data procedures, or a parallel result for another analysis population. The posted secondary outcomes add limited context but do not resolve the uncertainty in the primary result.

This is a statistical interpretation of the registry results, not guidance for treatment decisions. It does not address outcomes beyond those reported, nor does it establish what the results mean for any individual.

18. Why This Trial Matters Statistically

This trial is statistically instructive because the record presents both a sponsor-reported non-inferiority test and a recalculation from posted summary statistics. These are easy to conflate if only a p-value is noticed. They answer different questions, and the non-inferiority result depends on a margin that is not reported in the registry record. Keeping the analyses separate is essential to avoid claiming that the recalculation confirms or refutes the sponsor’s analysis.

The trial also illustrates why effect estimates and intervals belong beside p-values. The primary event counts are limited, and the recalculated risk-difference interval extends across the no-difference value. The point estimate gives a direction, but the interval conveys that a range of effects remains compatible with the posted data. The relative measures show similar uncertainty on their own scales.

The per protocol population and open-label design are also important parts of the interpretation. The registry identifies the analysis population but does not describe its detailed construction, missing-data handling, or procedures for outcome adjudication. Those omissions do not invalidate the posted results, but they constrain what can be assessed independently.

Finally, the planning illustrations show how strongly sample-size requirements depend on the effect a future study aims to detect. They use the observed effect and stated generic planning assumptions, not the original design assumptions for this trial. Distinguishing a planning illustration from a completed study’s design calculation helps prevent a retrospective calculation from being mistaken for evidence about the trial’s planned power.

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.

Several trial-specific limitations follow from the registry entries. The study was open-label, and the record does not describe whether outcome adjudication was blinded or how event classification was conducted beyond the confirmation requirements included in the endpoint definition. The primary endpoint is a composite, but component-specific primary results are not reported in the registry record. The total composite therefore cannot show which components contributed most to the observed counts.

The primary result is reported for the per protocol set, while the registry does not provide its full definition or a corresponding result for another analysis population. Missing-data handling, exclusions, adherence, and sensitivity analyses are not reported in the registry record. This makes it difficult to evaluate how participant selection and unavailable outcome information may have affected the estimate.

The sponsor’s non-inferiority analysis lacks its margin and further details in the record, limiting independent assessment or reproduction. The original sample-size justification and assumptions are also not reported. The planning illustration displayed alongside the results is based on the observed effect and stated generic assumptions, so it cannot fill that gap.

Secondary reporting is incomplete: the registry names rate of major VTE, but its result is not reported in the registry record. The record also does not describe a multiplicity strategy for interpreting multiple outcomes. Finally, the posted primary comparison has broad intervals, and safety summaries provide counts without further detail about timing, relatedness, or follow-up. These limitations frame what can be concluded from this registry record; they do not justify filling in absent protocol details by assumption.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Superficial Vein Thrombosis (SVT) Treated With Rivaroxaban Versus Fondaparinux — NCT01499953.
• Registry record last updated 2023-05-15; status last verified 2022-07.
• Results first posted 2023-05-15.
• 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

The registry describes a completed phase 3, randomized, open-label, parallel-group trial sponsored by GWT-TUD GmbH, with enrollment of 472. It compared 45 days of oral rivaroxaban, 10 mg OD, with 45 days of subcutaneous fondaparinux, 2,5 mg OD, for superficial vein thrombosis.

The primary efficacy endpoint was a composite of objectively confirmed VTE complications up to day 45, assessed in the per protocol set over 45 +/- 5 days. The sponsor reported an asymptotic non-inferiority test with p = 0.025. A recalculation from posted summaries gives a risk difference of -0.015, with interval -0.045 to 0.014 and unadjusted p-value 0.309. The record does not report the non-inferiority margin, limiting independent interpretation of the sponsor’s test.

Secondary and safety data provide additional descriptive information, but their reporting and analysis details are limited. The posted results should be interpreted with attention to the different analyses, the primary interval’s uncertainty, and the information not reported in the registry record.