The SOX Trial: Compression Stockings to Prevent the Post-Thrombotic Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The SOX Trial: Compression Stockings to Prevent the Post-Thrombotic Syndrome (NCT00143598), a randomized phase 3 study. The primary outcome is Incidence of Post-thrombotic Syndrome (PTS).

2. Clinical Question

The trial addressed prevention of PTS after symptomatic proximal DVT. The registry identifies PTS incidence as the primary outcome and gives the timeframe as during 2-year follow-up. It does not report the diagnostic criteria used to classify PTS, so the exact operational definition cannot be described from this record.

The comparison is between assignment to the two stocking groups, not simply between people who did and did not choose to wear stockings. The primary outcome is stated to use intention-to-treat, which generally means participants are analyzed according to their assigned group; details about how adherence and missing outcome information were handled are not reported.

3. Trial Design

The SOX Trial is listed as a phase 3, randomized, parallel-group study with triple masking. Its status is completed. The registry reports enrollment of 806 participants, a start date of 2004-06, and primary completion in 2012-02. The sponsor is Sir Mortimer B. Davis - Jewish General Hospital.

The two interventions were knee-length devices: active graduated elastic compression stockings and placebo stockings. The active stocking description specifies 30-40 mm Hg compression at the ankle. The placebo stocking was described as having an identical appearance and < 5 mm Hg compression at the ankle. The study summary describes the intended use period as 2 years. The registry does not describe adherence monitoring, instructions for use, or whether participants could receive other compression devices.

Random assignment is intended to make the groups comparable, on average, in both measured and unmeasured characteristics. A parallel design means participants are assigned to one group rather than crossing over between the two interventions as part of the design. These are general descriptions of the design terms; the registry record does not provide the randomization sequence-generation or allocation-concealment procedures.

The record labels masking as triple but does not identify which groups of people were masked or describe how masking was maintained. Those details are not reported in the registry record. The record reports 806 enrolled participants, while the primary endpoint listings give group denominators of 409 and 394. It does not explain the relationship between the enrollment figure and those endpoint denominators.

The registry lists three secondary outcome topics: PTS severity, including incidence of venous ulcer; objectively confirmed recurrent venous thromboembolism (VTE), death from VTE, and major bleeding; and quality of life. Their specific measurement schedules and definitions 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: Patients were excluded if they had a contraindication to the use of compression stockings, an expected life span of \<6 months, geographical inaccessibility, were unable to apply stockings, or received thrombolytic therapy for the initial treatment of acute deep vein thrombosis (DVT).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat.

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: 806 patients were randomly assigned to an intervention. Three patients were identified as ineligible soon after randomization and were excluded from further analysis (ie, modified intention-to-treat). In the active ECS group, one patient had no DVT and in the placebo ECS group one patient had a previous DVT and another patient was moribund.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Post-thrombotic Syndrome (PTS), measured over During 2-year follow up.

The primary endpoint is the incidence of post-thrombotic syndrome (PTS), expressed as the number of participants with the outcome during 2-year follow-up. The record describes the primary population as intention-to-treat. The posted group counts are 44 participants in the active ECS group and 37 in the placebo ECS group. The corresponding denominators are 409 and 394.

In general, incidence as a binary endpoint records whether each participant experienced the outcome during the specified period. It provides a direct comparison of the proportion of participants with the event in each group, without describing the timing of an event within follow-up. The record also includes a separate regression, Cox analysis expressed as a hazard ratio, which takes event timing into account in a time-to-event framework.

PTS is the condition the trial aimed to prevent after symptomatic proximal DVT, making its incidence relevant to the stated research question. The registry does not specify diagnostic criteria, assessment procedures, or how borderline cases were classified. It also does not report how participants without an observed outcome by the end of follow-up were handled in the binary endpoint analysis. These details affect how precisely the endpoint can be interpreted, and should not be inferred from the endpoint label alone.

7. Results Posted in the Registry

• Active ECS: 10.8% (44/409) versus 9.4% (37/394) on control; risk difference 1.4 percentage points (95% CI -2.8 to 5.5), risk ratio 1.15 (0.76–1.73); unadjusted two-proportion z-test p = 0.520.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: each participant either is or is not counted as having PTS during the stated follow-up. The registry reports the number of participants with the event and the group denominator. A basic unadjusted comparison uses these counts to estimate the risk in each group and contrasts those risks. The resulting risk difference is defined as active ECS minus placebo ECS. This is a simple summary of the observed group proportions; it does not adjust for other variables or use the event timing.

The re-calculated comparison is labeled unadjusted. In general, an unadjusted analysis compares groups without incorporating covariates such as baseline characteristics. Randomization supports a between-group comparison, but it does not make the unadjusted estimate a guarantee of balance in every observed characteristic. The registry does not report covariate adjustment for the primary count-based re-calculation.

A confidence interval describes a range of effect estimates compatible with the data under the analysis and its assumptions. It is not a range that contains a fixed percentage of individual participants' outcomes, nor is it a probability statement about whether the particular observed estimate is correct. For a risk difference, zero represents no difference between the group risks. The re-calculated interval crosses zero, and the reported unadjusted p-value is 0.52. In general, a p-value measures how unusual results at least this discrepant from a null model would be if that model and the analysis assumptions held. It does not measure the probability that the null hypothesis is true, or the clinical importance of an effect.

The registry also reports a regression, Cox analysis with a hazard ratio (HR). In general, a hazard ratio compares the instantaneous event rates between groups among participants who have not yet experienced the event, while accounting for the timing of events and censoring under the model. It is not the same quantity as a risk difference or a ratio of the final event proportions. The posted HR is 1.13, with a 95% confidence interval from .73 to 1.76 and p = .58. The registry does not describe the model covariates or provide further detail about its implementation.

For time-to-event data, some participants may have different observed follow-up times, and some may not experience the event during their observed follow-up. General survival-analysis methods use the timing information and account for incomplete event observation through censoring assumptions. The registry labels the method as regression, Cox, but does not give enough detail to assess those assumptions or specify censoring procedures. The count-based outcome and Cox analysis should therefore be interpreted as related but distinct summaries.

Why over-dispersion can matter

General explanation: over-dispersion occurs when variation in observed outcomes is greater than a chosen statistical model expects. If a model assumes less variation than the data contain, standard errors can be too small and intervals too narrow. The primary endpoint is a participant-level binary outcome, and no over-dispersion assessment is reported in the registry record. It should not be assumed that such an assessment was or was not performed.

What the reported analysis can establish

The primary counts, unadjusted re-calculation, and registry-reported Cox analysis describe the observed comparison and its statistical uncertainty. A p-value above a conventional threshold does not establish equivalence. An equivalence conclusion would require a prespecified equivalence margin and a design and analysis aimed at that question; such a margin and such an aim are not reported in the registry record. The registry record also does not report the trial's original sample-size justification, planned statistical analysis details, interim analyses, or any stopping rules.

The term intention-to-treat is used for the primary outcome population. In general, intention-to-treat analysis preserves the randomized comparison by analyzing participants according to allocation. The registry record does not explain how missing outcome data, withdrawals, protocol deviations, or participants with incomplete follow-up were handled. Accordingly, the stated population label should not be taken as a full account of those procedures.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data constrain the possible effect sizes. The count-based re-calculation has a confidence interval that extends on both sides of zero for the active-minus-placebo risk difference. That means the interval includes no difference and also allows differences in either direction. The point estimate alone is therefore not enough to describe what the data establish.

The registry-reported Cox estimate is HR 1.13, with a 95% confidence interval from .73 to 1.76. For a hazard ratio, 1 represents equal hazards under the model. The reported interval includes values below and above 1, so it is compatible with different directions of the relative time-to-event comparison as well as no difference. The reported p-value is .58. Neither the interval nor the p-value establishes that the groups have identical outcomes.

In general, a 95% confidence interval is produced by a procedure that, over repeated studies under its assumptions, would cover the target parameter in 95% of such intervals. For an individual study, it conveys uncertainty around the estimate rather than certainty about a single true value. Interval width depends on the amount of information and the variability of the data, as well as the analysis method. The available group counts and event counts provide context, but do not remove the uncertainty expressed by the intervals.

The risk-difference interval and the Cox interval refer to different effect measures and should not be compared as though they were on the same scale. The former concerns the difference in observed proportions over follow-up; the latter is a relative time-to-event measure. The registry does not provide further precision measures for other outcomes in the registry record.

11. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed primary effect, not the original trial design. They give participants per arm for 80% power and participants per arm for 90% power. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The original trial's sample-size assumptions and justification are not reported in the registry record.

At 100% of the observed effect, the illustration gives 7,609 participants per arm for 80% power and 10,185 participants per arm for 90% power. At 75% of the observed effect, it gives 13,323 participants per arm for 80% power and 17,835 participants per arm for 90% power. At 50% of the observed effect, it gives 29,516 participants per arm for 80% power and 39,513 participants per arm for 90% power.

In general, power is the probability that a specified statistical procedure will detect an effect of a chosen size if that effect is present, under the assumptions used for planning. The 80% column describes a planning target with an 80% chance of detecting the assumed effect, and the 90% column uses a higher detection-probability target. Smaller effects need more participants to detect under otherwise comparable assumptions, as illustrated by the increasing figures when the assumed effect is reduced from 100% to 75% and 50% of the observed effect. These are not observed power.

The planning table is expressed in participants per arm; these are not total event counts. The sample-size assumptions also specify equal allocation, so the values describe the size of each hypothetical group rather than the combined sample. A curve can be read as a visual representation of how the planning requirement changes with the assumed effect size; it does not change the assumptions or turn the illustration into a reconstruction of the trial's original design.

12. 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 = 0.094; treatment proportion p₁ = 0.108; average p̄ = 0.101.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4257 = 0.8343.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4256 = 0.3582.
4. n = (0.8343 + 0.3582)² / (0.0137)² = 7,608.2, rounded up to 7,609 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 <- 0.0939086294416244                          # control proportion
p1 <- 0.107579462102689                          # 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(143598)
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 = 7,609 (80% power), 10,185 (90% power)
 75% of observed effect: n per arm = 13,323 (80% power), 17,835 (90% power)
 50% of observed effect: n per arm = 29,516 (80% power), 39,513 (90% power)
power.prop.test: 7608.2 
Simulated power at n = 7,609 per arm: 0.803 (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.

13. Analyses Reported by the Sponsor

The registry-reported analysis is a regression, Cox analysis with HR 1.13, 95% confidence interval from .73 to 1.76, and p = .58. The re-calculation uses the posted binary event counts and denominators to make an unadjusted comparison of the observed risks. The two analyses address the same broad group comparison but use different effect measures and methods.

The Cox result concerns relative event rates over time under the model, while the risk-difference re-calculation concerns the difference between the proportions with an event during the stated follow-up. The registry does not provide the Cox model's covariates, detailed specification, or diagnostics. It is therefore not possible to identify from the registry record exactly how the sponsor's model was implemented beyond the method label and reported estimate.

The re-calculated result is not a replacement for the registry-reported analysis. It is a transparent, unadjusted calculation from the posted summary counts, while the sponsor-reported result is the analysis recorded by the trial. Their distinct scales and analytic approaches mean that their estimates should not be expected to match numerically. Both reported statistical summaries have uncertainty compatible with no difference; neither establishes equivalence or proves absence of an effect.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three secondary outcome topics in addition to the primary PTS endpoint: PTS severity, including incidence of venous ulcer; objectively confirmed recurrent VTE, death from VTE, and major bleeding; and quality of life. It reports four outcome measures and one analysis in the posted results. The registry entries do not include results for the secondary outcomes.

When several outcomes or comparisons are tested, the chance of obtaining at least one apparently notable result by chance can increase. General statistical practice may address this through a prespecified hierarchy, adjustment for multiple testing, or clear distinction between confirmatory and exploratory analyses. The registry record does not report a multiplicity strategy, a hierarchy among outcomes, or whether secondary outcomes were considered confirmatory. It is not possible to infer that an adjustment was or was not used.

The record identifies the primary outcome population as intention-to-treat. It does not detail the analysis population for the Cox model or secondary outcomes. Information about missing data, withdrawals, incomplete follow-up, exclusions, protocol deviations, and imputation is not reported in the registry record. Nor does the record specify how participants with unavailable outcome assessments were classified in the binary endpoint analysis.

The trial's statistical analysis plan, original sample-size justification, interim analyses, and stopping rules are not reported in the registry record. The planning illustration based on the observed effect is not evidence of the original design assumptions. These absences limit assessment of whether the posted analysis follows a prespecified plan and how robust the findings are to missingness or choices among multiple outcomes.

15. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event entries report 0 affected participants among 409 at risk in the active ECS group and 0 among 394 at risk in the placebo ECS group. The other adverse event entries report 8 affected participants among 409 at risk in the active group and 7 among 394 at risk in the placebo group.

These figures are counts recorded in the registry. They do not, by themselves, describe event severity beyond the serious-versus-other classification, event timing, duration, recurrence, or whether an event was judged related to a stocking. The record does not provide the definitions used for these categories or a breakdown of the other adverse events.

The death entries have no reported counts, and no serious adverse event terms are listed. An absent death count is not the same as a reported count of zero. These entries do not support conclusions beyond what is recorded, and the adverse event figures should not be treated as a complete account of the trial's safety findings.

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

The central finding is that the posted primary event counts were 44 participants in the active ECS group and 37 in the placebo ECS group, with denominators of 409 and 394. The unadjusted comparison has a p-value of 0.52 and a confidence interval that crosses zero. The registry-reported Cox result is HR 1.13, with a 95% confidence interval from .73 to 1.76 and p = .58. These analyses do not show a clear statistical difference between the groups in the primary outcome.

That conclusion is narrower than saying the interventions are equivalent or that there is no effect. The uncertainty intervals allow effects on either side of the no-difference value. A result that does not establish a difference can occur when the true effect is small, when the estimate is imprecise, or for other reasons; the registry results alone do not distinguish among these possibilities. The trial's original design assumptions are not reported, so the sample-size illustration cannot be used to characterize the trial's planned ability to detect an effect.

The primary result concerns PTS incidence during 2-year follow-up in the stated intention-to-treat population. It does not answer every question about PTS severity, venous ulcers, recurrent VTE, death from VTE, major bleeding, or quality of life. Although the record names those as secondary outcomes, their results are not included in the information.

The endpoint definitions and details of outcome ascertainment are also not available in the registry record. As a result, the counts can be described as posted, but the diagnostic and assessment procedures cannot be independently characterized from this record. The Cox analysis adds a time-to-event summary, but its model details are likewise not reported.

These findings should be understood as a comparison in the recorded trial population, using the named stockings and stated follow-up. They do not establish conclusions about other populations, devices, durations, or clinical decisions. No treatment recommendation follows from these statistics alone.

17. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. A binary endpoint can be summarized by the number of participants experiencing an event and a risk difference over a fixed follow-up period. A Cox model instead uses event timing and reports a hazard ratio. These summaries answer related but distinct statistical questions, so a reader should identify the scale before interpreting an estimate.

It also illustrates the importance of reading an estimate together with its interval. The primary re-calculation has a confidence interval extending across zero, and the reported Cox interval extends across 1, the no-relative-hazard value. The p-values do not establish a clear group difference, but neither do the intervals demonstrate equivalence. Statistical interpretation requires both the direction of the point estimate and the range of effects compatible with the data.

The trial record further distinguishes a sponsor-reported analysis from a simple unadjusted re-calculation. The latter can make use of published group counts, but it cannot reproduce model details that are not recorded. Transparency about the analysis scale, population, and uncertainty is essential when comparing results.

Finally, planning illustrations based on the observed effect are not the same as a trial's original sample-size rationale. They can show how assumed effect size and desired power influence planning requirements, while leaving unanswered what the investigators planned before the data were observed. Keeping those questions separate prevents retrospective planning calculations from being mistaken for evidence about the original design.

18. Limitations

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

The registry record gives a compact outcome description but does not specify the diagnostic criteria or assessment procedures for PTS. Without those details, the primary event counts cannot be linked to a more exact operational definition or to a particular assessment method.

The record reports both a binary primary outcome and a Cox analysis, but the Cox model specification is not described beyond the regression, Cox label. Covariates, model checks, censoring procedures, and assumptions are not reported. The count-based re-calculation is unadjusted and cannot substitute for unavailable model details.

The recorded endpoint denominators are 409 for active ECS and 394 for placebo ECS, while enrollment is 806. The registry does not explain the relationship among these figures. It also does not describe missing outcome data, withdrawals, follow-up completeness, adherence, or how deviations from assigned treatment were handled.

The registry lists secondary outcomes but the results include no secondary outcome findings. Multiplicity procedures, the original sample-size justification, interim analyses, and stopping rules are not reported in the registry record. These gaps limit a complete evaluation of the planned analysis, secondary findings, and potential sensitivity of results to analytic choices.

The safety entries are also limited: the record gives group counts for serious and other adverse events, but does not provide event descriptions for the other category, attribution, timing, or death counts. These limitations are specific to the detail available in this registry record and should not be filled in by assumption.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The SOX Trial: Compression Stockings to Prevent the Post-Thrombotic Syndrome — NCT00143598.
• Registry record last updated 2014-08-18; status last verified 2014-08.
• Results first posted 2014-08-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The SOX Trial (NCT00143598) is a completed phase 3 randomized, triple-masked, parallel-group study sponsored by Sir Mortimer B. Davis - Jewish General Hospital. The registry lists enrollment of 806, a start date of 2004-06, and primary completion in 2012-02.

It compared active knee-length graduated ECS with placebo stockings after symptomatic proximal DVT. The primary endpoint was PTS incidence during 2-year follow-up in the intention-to-treat population. The posted counts were 44 of 409 in the active group and 37 of 394 in the placebo group. The registry-reported Cox analysis gave HR 1.13, 95% confidence interval .73 to 1.76, and p = .58. The record also lists three secondary outcome topics, with their results not described in the information.