Rivaroxaban With Diosmin in Long-term Treatment of Deep Vein Thrombosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rivaroxaban With Diosmin in Long-term Treatment of Deep Vein Thrombosis (NCT03413618), a randomized phase 4 study. The primary outcome is Number of Participants With Postthrombotic Syndrome as Determined by Villalta Score.

2. Clinical Question

This question focuses on whether the randomized groups differed in the occurrence of postthrombotic syndrome during the stated follow-up. The registry describes the Villalta score as combining subjective symptoms and objective signs of chronic venous disease, with higher scores reflecting greater severity. It also distinguishes mild, moderate and severe syndrome by score ranges. Those severity categories provide clinical context, but the posted primary outcome is the number of participants meeting the overall threshold, rather than a comparison of severity categories.

The comparison is specifically about adding diosmin to rivaroxaban and compression stockings in this trial setting. It does not isolate the effect of diosmin in the absence of those other treatments. Nor does the primary result answer every question about recurrence, symptoms, quality of life or safety; those were addressed through secondary outcomes, some of which have posted results and others for which results are not reported in the registry record.

3. Trial Design

The registry describes a completed, randomized, single-masked, parallel-group phase 4 study. Its title concerns rivaroxaban with diosmin in long-term treatment of deep vein thrombosis, and its official title specifies acute proximal deep vein thrombosis. The stated enrollment was 90. The experimental arm was rivaroxaban plus diosmin plus compression stockings, and the control arm was rivaroxaban plus compression stockings only. The posted primary outcome has 45 participants recorded in each arm.

The study start date was 2017-12-20, and the primary completion date was 2019-07-31. The sponsor was Pirogov Russian National Research Medical University. The registry status is completed. The registry identifies the study as phase 4, but additional details about the development or regulatory context are not reported in the registry record.

Random allocation supports a between-group comparison by assigning participants to treatment regimens rather than allowing the groups to be selected entirely by clinical choice. The registry labels masking as single, but does not report which people were masked or how masking was maintained. It also does not report the randomization method, allocation concealment procedures, recruitment setting, eligibility criteria, treatment adherence, or protocol deviations. Those details should not be inferred from the design labels alone.

The stated aim was to assess efficacy and safety, with particular interest in the speed of deep vein recanalization and the incidence of postthrombotic syndrome. The primary outcome is postthrombotic syndrome at 12 months. The registry lists 11 outcome measures and six analyses. Ten secondary outcomes are posted in the results information, while detailed result summaries are available for only some of them. The original sample-size justification, the original statistical analysis plan and any interim analysis plans are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Admitted to the hospital with the suspicion for DVT: 202; DVT verified: 158; Eligible DVT: 102; Rejected to participate: 12; Randomized: 90

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Postthrombotic Syndrome as Determined by Villalta Score, measured over 12 months.

The primary endpoint is the number of participants with postthrombotic syndrome at 12 months, determined using the Villalta score. The registry describes that score as a combination of subjective symptoms and objective signs of chronic venous disease. Its stated range is 0 to 33, with higher values representing greater severity. The record defines postthrombotic syndrome as a score of 5 and more; it classifies scores of 5-9 as mild, 10-14 as moderate and 15 and more as severe.

Using a defined threshold turns the score into a participant-level event: a participant either meets the stated definition or does not. That makes the primary outcome interpretable as a count and allows the randomized groups to be compared on the proportion meeting the threshold. As a general statistical point, a threshold can make a complex symptom-and-sign assessment easier to summarize, but it also means that differences in score values within the same category are not reflected in the event count.

The endpoint is relevant to the study’s stated focus on postthrombotic syndrome after deep vein thrombosis. It is not a direct measure of every aspect of venous health or of treatment safety. The registry identifies the timeframe as 12 months, but does not report additional assessment timing, the procedures for scoring or adjudication, or how missing Villalta assessments were handled.

7. Results Posted in the Registry

• Experimental: Rivaroxaban + Diosmin + Stockings: 6.7% (3/45) versus 48.9% (22/45) on control; risk difference -42.2 percentage points (95% CI -58.5 to -25.9), risk ratio 0.14 (0.04–0.42); 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 Participants With Recurrent Symptomatic or Asymptomatic DVT

• 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:
  • Experimental: Rivaroxaban + Diosmin + Stockings: 2.2% (1/45) versus 13.3% (6/45) on control; risk difference -11.1 percentage points (95% CI -21.9 to -0.3), risk ratio 0.17 (0.02–1.33); unadjusted two-proportion z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Experimental: Rivaroxaban + Diosmin + Stockings than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The Value of Venous Clinical Severity Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Experimental: Rivaroxaban + Diosmin + Stockings: mean 1.20 versus 4.40 on control; difference -3.20 (95% CI -3.89 to -2.51), standardized effect d = -1.91; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Experimental: Rivaroxaban + Diosmin + Stockings than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The Value of Chronic Lower Limb Venous Insufficiency Questionnaire - 20 Items

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Experimental: Rivaroxaban + Diosmin + Stockings: mean 22.10 versus 28.80 on control; difference -6.70 (95% CI -9.12 to -4.28), standardized effect d = -1.14; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Experimental: Rivaroxaban + Diosmin + Stockings than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The direction of the posted secondary results is broadly aligned with the primary comparison: the experimental group has fewer recorded recurrences and lower reported average scores for venous clinical severity and venous insufficiency. This coherence across outcomes gives context to the primary postthrombotic-syndrome result, because the measures address related but distinct aspects of deep vein thrombosis and its consequences. They are not interchangeable outcomes, and agreement in direction does not establish that each result is independently conclusive.

The registry lists additional secondary outcomes, including symptomatic pulmonary embolism, full popliteal vein recanalization, residual venous obstruction, adverse events and major bleeding. Results for these listed outcomes are not reported in the registry record. The registry reports 10 secondary outcomes as posted, but the detailed summaries available for several measures do not describe the full secondary-outcome set. As a result, the direction and precision of the overall secondary evidence cannot be fully assessed from the registry record.

Secondary outcomes generally carry less evidential weight than a prespecified primary outcome when their testing strategy and multiplicity handling are not reported. As a general statistical point, assessing many outcomes increases the chance that some results will appear notable by chance. The registry does not report a multiplicity adjustment, a hierarchy for secondary testing or a complete analysis plan. The secondary findings are therefore best treated as supportive context and as outcomes requiring cautious interpretation, rather than as a set of independent confirmations.

The outcome measures also differ in type and scale. A recurrence count, a clinical severity score and a questionnaire score capture different information, and their effect estimates cannot be compared directly by magnitude. Their shared direction is a descriptive pattern, not proof that all domains changed by the same amount or through the same mechanism.

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

• Number of Participants With Recurrent Symptomatic or Asymptomatic DVT
• Number of Participants With Symptomatic Pulmonary Embolism
• The Value of Venous Clinical Severity Score
• The Value of Chronic Lower Limb Venous Insufficiency Questionnaire - 20 Items
• Number of Participants With Full Recanalization of the Popliteal Vein
• Extension of Residual Venous Obstruction by Marder Score
• Adverse Events
• Major Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary comparison is an unadjusted risk difference: the event risk in the experimental arm minus the event risk in the control arm. A negative estimate means the recorded event risk was lower in the experimental group. The estimate of -0.422 is a difference on the risk scale. It is not a relative risk, an odds ratio or a count difference. The comparison uses the reported arm counts and the posted arm sizes; it does not adjust for baseline characteristics or other variables.

As a general statistical explanation, a risk difference keeps the comparison on an absolute scale. It describes the separation in event probability between groups, while a relative measure describes one group’s risk in relation to the other. The registry also contains relative effect measures for the primary outcome, but the risk difference is the measure used for the recalculated primary comparison discussed in the interpretation.

How should a confidence interval be understood?

A confidence interval describes the range of effect estimates reasonably compatible with the observed data under the assumptions of the calculation. It conveys uncertainty around an estimate rather than the range of individual participant outcomes. For the primary risk difference, the interval runs from -0.585 to -0.259. Because its values are all negative, it is consistent with a lower observed risk in the experimental group under this unadjusted comparison. The interval does not account for unreported sources of uncertainty such as missing outcomes, measurement issues or deviations from the study procedures.

As a general concept, a confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it assign a probability to the treatment effect after the data have been observed. Its width reflects statistical precision under the chosen method and data. A narrow interval can still be affected by bias, and an interval that excludes the null value does not resolve limitations in study design or reporting.

What does a p-value contribute?

The recalculated p-value for the primary outcome is <0.001, while the sponsor’s reported Fisher Exact result is p < 0.001. A p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of the effect.

The sponsor reports Fisher Exact for the primary comparison. This is an exact test commonly used for categorical outcomes, including event counts in groups. The recalculated estimate and interval use unadjusted summary statistics. The registry record does not report the full specification of the sponsor’s analysis beyond the named method, reported p-value and superiority label.

How are the secondary outcome methods different?

Recurrence is also recorded as a participant count and has a recalculated risk difference. The sponsor’s reported method for that outcome is Log Rank. As a general explanation, a log-rank test compares event experience over time rather than only comparing whether an event was recorded by a single endpoint time. The registry record does not provide the event-time data, censoring details or other specifications needed to independently reconstruct that analysis.

Venous Clinical Severity Score and Chronic Lower Limb Venous Insufficiency Questionnaire scores are reported as means with standard deviations. Their recalculated comparisons are mean differences, which express the difference between group averages on the score scale. A mean difference is not a difference in event risk. The registry labels the sponsor’s reported analyses for these outcomes as Fisher Exact, even though the outcomes are presented as continuous scores. The record does not provide enough detail to determine how those reported tests were applied or whether they correspond to a categorization not otherwise described.

As a general statistical point, averages can conceal variation among participants and may be influenced by skewed distributions or outlying values. Standard deviations describe variation around group means; they are not confidence intervals for the means. The registry does not report distributional checks, transformations, covariate adjustment or alternative analyses for the continuous outcomes.

What does “unadjusted” mean in this analysis?

The recalculated comparisons are simple, unadjusted re-calculations from posted summary statistics. They do not incorporate participant-level covariates, stratification variables or any adjustment for the number of outcomes assessed. An unadjusted result is not necessarily invalid, but it answers a narrower question than a prespecified adjusted analysis could answer. The original analysis plan and its prespecified methods are not reported in the registry record.

As a general statistical consideration, testing multiple outcomes creates more opportunities for apparently notable results by chance. Adjustment methods can address some forms of multiplicity, but no adjustment method is reported in the registry record. The sponsor’s analysis takes precedence for the trial’s reported results; the recalculated results are useful for describing posted summaries, not for replacing an unavailable full analysis plan.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.422, with a confidence interval from -0.585 to -0.259. The interval lies on the negative side of zero and does not include zero, indicating that the posted data distinguish the groups on the unadjusted risk-difference scale under the calculation used. The interval still spans a range of possible effect magnitudes, so the point estimate should not be treated as an exact or uniquely determined value.

For the primary endpoint, the observed counts were 3 and 22, with 45 participants recorded in each arm. The event counts are substantially separated, but the interval remains important: it conveys uncertainty that a single point estimate does not. The interval is not a prediction interval for what would happen to individual participants, and it does not capture possible bias arising from unreported missing data or outcome-assessment procedures.

Precision also varies across endpoints. The recurrence risk-difference interval is -0.219 to -0.003, close to zero at its upper endpoint. The interval for the Venous Clinical Severity Score mean difference is -3.893 to -2.507, and for the venous insufficiency questionnaire mean difference it is -9.121 to -4.279. These intervals reflect the scales and summary measures of their respective outcomes and should not be compared as if they were measured in the same units.

As a general interpretation, statistical precision is only one part of evidential strength. The intervals describe sampling uncertainty under the calculation’s assumptions; they do not address multiplicity, missing outcomes, measurement reliability, generalizability or unreported design details. The registry record does not report adjusted confidence intervals or a full analysis plan for these outcomes.

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 estimates are planning illustrations based on the observed effects, not the trial’s original design justification. For binary outcomes, the entries are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. For time-to-event outcomes, the stated convention is total events; for other outcomes, the estimates are participants per arm. The original design assumptions are not reported in the registry record.

Each planning row represents a different fraction of the observed effect: 100%, 75% or 50%. The columns labeled for 80% and 90% power indicate the participants per arm estimated to give those chances of detecting the specified effect under the stated assumptions, if the assumptions hold. Power is a property of a planned design under a chosen effect and analysis, not a probability that a trial result is correct.

For the primary outcome, the estimate for 100% of the observed effect is 17 participants per arm for 80% power and 22 participants per arm for 90% power. Planning for 75% of the observed effect gives 34 participants per arm for 80% power and 45 participants per arm for 90% power. Planning for 50% of the observed effect gives 83 participants per arm for 80% power and 110 participants per arm for 90% power. The required sample size rises as the effect to be detected becomes smaller, because a smaller group difference is harder to distinguish from random variation.

The sample-size curve is read as the relationship between the effect size assumed for planning and the resulting sample-size requirement: moving toward smaller effects means a larger requirement. These figures are not observed power, and they do not establish that the study was adequately powered under its original plan. They are retrospective illustrations calculated from observed effects, which can be unstable as planning targets.

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 = 0.489; treatment proportion p₁ = 0.067; average p̄ = 0.278.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6334 = 1.2415.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5587 = 0.4702.
4. n = (1.2415 + 0.4702)² / (-0.4222)² = 16.4, rounded up to 17 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 <- 0.488888888888889                          # control proportion
p1 <- 0.0666666666666667                          # 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(3413618)
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 = 17 (80% power), 22 (90% power)
 75% of observed effect: n per arm = 34 (80% power), 45 (90% power)
 50% of observed effect: n per arm = 83 (80% power), 110 (90% power)
power.prop.test: 16.4 
Simulated power at n = 17 per arm: 0.835 (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 reported primary analysis compares the randomized groups using Fisher Exact and labels the result as superiority, with p < 0.001. The recalculated primary comparison is an unadjusted risk difference of -0.422, with a confidence interval from -0.585 to -0.259 and p <0.001. The recalculation is based on the posted summary counts and is not a reconstruction of the complete sponsor analysis.

The two p-values are expressed at different levels of precision. Both indicate that the observed primary data are inconsistent with a null difference under their respective analyses, but the sponsor’s reported analysis takes precedence when describing the trial’s own inferential result. The recalculated estimate and interval add an effect-size description on the risk-difference scale; they do not replace the sponsor’s analysis or show that the sponsor used the same method for estimating the effect.

The registry record does not report a sponsor-estimated risk difference or its confidence interval, nor does it provide all details of the analysis specification. The recalculated statistics therefore should be read as simple unadjusted calculations from the posted arm summaries. They do not establish whether the sponsor’s analysis adjusted for other factors, followed a prespecified hierarchy, or used a particular analysis population. The original statistical analysis plan is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the sponsor adjusted for testing multiple outcomes, used a prespecified testing hierarchy or designated any secondary outcomes as confirmatory. It lists 11 outcome measures and six analyses, and 10 secondary outcomes are posted. Without the analysis plan, it is not possible to determine whether the reported p-values were intended as independent tests, whether some outcomes were exploratory, or whether a family-wise error or false-discovery procedure was used.

As a general statistical explanation, multiplicity matters because each additional hypothesis test creates another opportunity for a result to appear statistically notable through chance variation. This does not mean that every secondary result is false; it means that an unadjusted p-value should be interpreted in the context of all the outcomes and analyses considered. The posted secondary results are therefore less definitive when no multiplicity strategy is reported.

Missing-data handling is not reported in the registry record. The posted primary and secondary arm summaries give participant counts, but they do not establish whether all randomized participants were included in every endpoint analysis, how unavailable assessments were handled, or whether outcomes were imputed. Analysis populations are also not reported. It is therefore not possible to confirm from the registry record whether the analyses used an intention-to-treat population, a per-protocol population or another definition.

The record does not report a detailed statistical analysis plan, interim analyses, covariate adjustment or sensitivity analyses for missing outcomes. These omissions limit assessment of whether the analysis followed prespecified procedures and how robust the results are to alternative assumptions. They do not negate the posted estimates, but they restrict the conclusions that can be drawn about their reliability beyond the reported summaries.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the study group and zero in the control group. It records other adverse events for 5 participants in the study group and 4 in the control group. Deaths are reported as zero in both groups. The serious adverse event counts are therefore the same in the two groups in the posted record; the other adverse-event counts are also close in absolute terms.

These figures are counts, not a complete description of the type, timing, severity or duration of every event. The record does not list serious adverse-event terms, and it does not report detailed information about attribution, treatment discontinuation or event follow-up. It also does not provide enough information to determine whether every participant had the same duration of safety observation.

As a general statistical point, a lack of recorded serious events in a trial does not establish that a regimen has no serious risks. Safety counts from a trial of this size may be imprecise for uncommon outcomes, and interpretation depends on the completeness of reporting and follow-up. These registry figures describe the events recorded in this study; they are not medical advice or a comprehensive safety assessment.

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

The primary result describes a clear separation in the recorded frequency of postthrombotic syndrome at 12 months between the randomized groups. The risk-difference estimate is negative for the experimental regimen, and its confidence interval excludes zero. The registry’s own reported primary analysis also gives a small p-value. Taken together, these statistics characterize the observed trial result, not a guarantee about results in every population or treatment setting.

The study compared adding diosmin to rivaroxaban and compression stockings against rivaroxaban and stockings alone. It does not estimate the effect of diosmin without anticoagulation or compression, and it does not compare rivaroxaban with a different anticoagulant. The randomized contrast is limited to the regimens described in the record.

The primary outcome is a threshold-based Villalta score classification. It records whether participants met the registry definition of postthrombotic syndrome, but it does not show the full distribution of scores, changes in score over time or the experience of each participant. The secondary score and questionnaire outcomes add related context, while the unreported secondary results leave other clinical questions unanswered.

The result does not show that every participant in the experimental group avoided postthrombotic syndrome, or that every participant in the control group experienced it. It does not establish long-term outcomes beyond the stated 12-month timeframe. It also does not settle questions about adherence, subgroup differences, missing assessments, treatment discontinuation, rare harms or generalizability, because the registry record does not report the details needed to evaluate them.

Statistical evidence and clinical importance are related but distinct. The p-value is not a measure of benefit size, and the confidence interval does not determine whether a difference is important to patients. The registry does not provide a threshold for clinically meaningful change or enough information to assess all dimensions of patient experience. The appropriate reading is descriptive: the posted data favor the experimental group on the primary event count in this trial, subject to the stated limits of the record.

18. Why This Trial Matters Statistically

This trial illustrates the value of separating the treatment contrast from the outcome definition. The randomized comparison is not diosmin versus no treatment; it is the addition of diosmin to a regimen containing rivaroxaban and compression stockings. A clear description of that contrast helps prevent attributing the entire group difference to a component that was not studied in isolation.

It also shows why effect estimates, intervals and p-values answer different questions. The risk difference describes the size and direction of the observed group separation on an absolute scale. Its confidence interval conveys uncertainty around that estimate. The p-value addresses compatibility with a null comparison under the test assumptions. None of these statistics alone resolves missing-data, multiplicity or generalizability concerns.

The posted primary and secondary measures span event counts, clinical severity and a patient-reported questionnaire. Their consistent direction is informative as a pattern, but differing scales and analytic methods mean that the results should not be combined casually. Unreported secondary results and an unavailable multiplicity strategy further limit how strongly the secondary findings can reinforce the primary result.

Finally, the registry record distinguishes sponsor-reported analysis from simple unadjusted recalculation. The sponsor’s reported primary test remains the trial’s own analysis, while the recalculated risk difference and interval help make the magnitude and precision easier to interpret. This distinction is important when summary data are available without a full protocol, statistical analysis plan or participant-level dataset.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification or the assumptions used to plan enrollment. The retrospective planning illustrations based on observed effects cannot establish whether the original design was adequately sized. The full statistical analysis plan, including prespecified adjustment methods and analysis populations, is also not reported.

Details needed to assess conduct and potential bias are missing. The record does not identify who was masked, how randomization and allocation concealment were implemented, or whether outcome assessors were masked. It does not report eligibility criteria, recruitment details, baseline characteristics, treatment adherence, protocol deviations or treatment discontinuations. These omissions restrict assessment of internal validity and applicability.

Missing-outcome procedures are not reported. The arm summaries do not establish whether all randomized participants contributed data to each outcome, nor how incomplete follow-up was handled. The registry also does not provide detailed information on the Villalta assessment process, score reliability or adjudication. These matters are particularly relevant when the primary endpoint depends on a scored assessment.

Only some of the listed secondary outcomes have detailed results. The record does not report results for several clinically relevant listed measures, and it does not state how multiplicity was managed. Safety reporting is limited to event counts without detailed terms or timing. The study’s results therefore cannot fully characterize the broader benefit-risk profile or resolve every outcome in the stated study aims.

Finally, the posted comparison is specific to the study’s regimen and 12-month primary timeframe. The record does not report longer-term follow-up or subgroup analyses. The observed estimates should not be extrapolated beyond the enrolled trial population and treatment contrast without additional evidence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Rivaroxaban With Diosmin in Long-term Treatment of Deep Vein Thrombosis — NCT03413618.
• Registry record last updated 2021-02-04; status last verified 2019-07.
• Results first posted 2020-01-27.
• 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

The registry describes a completed, randomized, single-masked, parallel-group phase 4 study sponsored by Pirogov Russian National Research Medical University. It enrolled 90 participants and compared rivaroxaban, diosmin and compression stockings with rivaroxaban and stockings alone. The primary outcome was postthrombotic syndrome by Villalta score at 12 months.

The posted primary counts were 3 participants in the experimental arm and 22 in the control arm, with 45 recorded in each arm. The recalculated unadjusted risk difference was -0.422, with a confidence interval from -0.585 to -0.259; the sponsor reported Fisher Exact p < 0.001. Several secondary results follow the same direction, but results for other listed outcomes are not reported in the registry record. Missing-data procedures, analysis populations, multiplicity handling and the original design assumptions are not reported.