Odiparcil For The Prevention Of Venous Thromboembolism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Odiparcil For The Prevention Of Venous Thromboembolism (NCT00244725), a randomized phase 2 study. The primary outcome is Percentage of Participants With Total VTE Event Over 10 ± 2 Days of Treatment.

2. Clinical Question

The outcome included adjudicated asymptomatic DVT detected at early withdrawal or after 8-12 days of treatment and no later than 1 day after treatment ended, as well as symptomatic DVT or PE during treatment and death adjudicated as related to VTE during treatment. It therefore combines events that differ in symptoms and ascertainment. A participant who remained asymptomatic at the end of the study did not have to undergo a mandatory bilateral venogram under the described procedure.

The study’s stated purpose was to examine odiparcil for prevention of blood clots after total knee replacement and to evaluate safety. The registry identifies the trial as Phase 2. The result describes the recorded outcome in this trial population and time period; it does not by itself establish how the findings apply to other populations, procedures, durations, or clinical decisions.

3. Trial Design

The registry describes a randomized, double-masked Phase 2 trial sponsored by GlaxoSmithKline. The recorded start was 2005-09, primary completion was 2006-09, and status is completed. Enrollment is listed as 961. These are registry entries; the record does not report the randomization sequence method, concealment procedure, masking procedures, or allocation ratio.

Four treatment groups have primary outcome results: Odiparcil MR 250 mg Tablet, Odiparcil MR 375 mg Tablet, Odiparcil MR 500 mg Tablet, and Warfarin INR 2.0 to 3.0. The registry’s model field says “single group,” which does not readily align with the randomized classification and the multiple reported treatment groups. The record does not explain this metadata discrepancy, so the study structure should be described using both the recorded design classification and the actual groups listed in the results rather than assuming why the fields differ.

The primary endpoint was assessed up to Visit 7, at 10 ± 2 days of treatment. According to the endpoint description, assessment could occur at study visits, at the end of study, or at early withdrawal. For asymptomatic participants completing the study, a bilateral venogram was not mandatory. Early withdrawals with VTE objectively confirmed by a method other than venography did not have to undergo venography. These procedures matter because the endpoint combines clinical events and events identified through imaging, with opportunities for detection affected by assessment procedures.

Several details needed to reconstruct trial conduct are not reported in the registry record. These include the planned allocation ratio, the original sample-size justification, the detailed statistical analysis plan, and the handling of protocol deviations. The registry also does not explain the mismatch between enrollment and the group-specific denominators used for the primary outcome.

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: A total of 958 participants were randomized into the study. Two participants each from the treatment arm Odiparcil 250 milligram (mg), and Odiparcil 375 mg did not receive the study medication. Therefore, the intent to treat (ITT) population was comprised of 954 participants.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population comprised of all participants who were randomized and received at least one dose of study treatment. Total number of participants with objectively confirmed symptomatic VTE, venographically detected VTE at early withdrawal or an evaluable venogram at study completion were used for analysis.

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 Percentage of Participants With Total VTE Event Over 10 ± 2 Days of Treatment, measured over Up to Visit 7 (10 ± 2 days of treatment).

The primary endpoint is the percentage of participants with a total VTE event over 10 ± 2 days of treatment, assessed up to Visit 7. A participant counted as having an event if the specified adjudicated criteria were met: asymptomatic DVT detected at early withdrawal or in the specified period after treatment, symptomatic DVT or PE during study treatment, or death adjudicated as related to VTE during treatment. The endpoint description identifies the Independent Central Adjudication Committee as the body adjudicating events.

This composite endpoint captures more than one way a VTE event might be identified. Symptomatic DVT and PE are clinical events, whereas asymptomatic DVT can be identified through venography. The registry states that an asymptomatic participant completing the study did not necessarily undergo a mandatory bilateral venogram. That qualification is important when interpreting an endpoint that includes imaging-detected events: detection depends in part on whether and when imaging was performed.

As a percentage endpoint, the result expresses the proportion of the analyzed group meeting the event definition, rather than the timing of events or their severity. It is useful for comparing the recorded event frequency across groups over the stated treatment period. It does not distinguish the component events in the primary result, and it should not be read as a complete account of symptomatic events, safety, or longer-term outcomes. The registry’s description of the primary population begins with participants randomized and given at least one dose, but the remaining text describing the denominator is incomplete. Additional detail on the exact analysis population and missing outcome handling is not reported in the registry record.

7. Results Posted in the Registry

• Odiparcil MR 375 mg Tablet: 44.4% (75/169) versus 45.1% (74/164) on control; risk difference -0.7 percentage points (95% CI -11.4 to 9.9), risk ratio 0.98 (0.77–1.25); unadjusted two-proportion z-test p = 0.892.
• Odiparcil MR 500 mg Tablet: 41.2% (66/160) versus 45.1% (74/164) on control; risk difference -3.9 percentage points (95% CI -14.7 to 6.9), risk ratio 0.91 (0.71–1.17); unadjusted two-proportion z-test p = 0.482.
• Warfarin INR 2.0 to 3.0: 31.2% (49/157) versus 45.1% (74/164) on control; risk difference -13.9 percentage points (95% CI -24.4 to -3.4), risk ratio 0.69 (0.52–0.92); unadjusted two-proportion z-test p = 0.010.

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.

Percentage of Participants With Total Asymptomatic VTE Over 10 ± 2 Days of Treatment

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Odiparcil MR 375 mg Tablet: 43.8% (74/169) versus 42.1% (69/164) on control; risk difference 1.7 percentage points (95% CI -8.9 to 12.3), risk ratio 1.04 (0.81–1.33); unadjusted two-proportion z-test p = 0.752.
  • Odiparcil MR 500 mg Tablet: 40.0% (64/160) versus 42.1% (69/164) on control; risk difference -2.1 percentage points (95% CI -12.8 to 8.6), risk ratio 0.95 (0.73–1.23); unadjusted two-proportion z-test p = 0.704.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Odiparcil MR 375 mg Tablet and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Odiparcil MR 500 mg Tablet and the control. The interval gives the range of effects that remain compatible with the data.

The registry reports 11 secondary outcomes, covering proximal and distal DVT, PE, VTE-related death, asymptomatic and symptomatic VTE, trough anti-IIa activity, and major bleeding, among other listed measures. These outcomes address different aspects of thrombosis, pharmacology, and safety. They do not all measure the same event or use the same scale, so a coherent interpretation requires attention to each outcome’s definition and assessment period.

The posted secondary result for total asymptomatic VTE has group percentages and confidence intervals, with recalculated comparisons against the 250 mg group. Its general pattern is consistent with the broader need to distinguish the composite primary endpoint from its components: asymptomatic events are only one part of the primary endpoint, and the primary endpoint also includes symptomatic events and VTE-related death. The registry does not post sponsor-reported analyses for this secondary endpoint.

Secondary endpoints can help describe whether the primary pattern is accompanied by similar findings in related outcomes, or whether the components differ. They should not be treated as independent confirmation of the primary result, particularly when many outcomes and comparisons are examined. In general, repeated testing increases the chance of finding apparently notable results by chance if no multiplicity strategy is applied. Whether the sponsor used a hierarchy, adjustment, or other multiplicity plan is not reported in the registry record.

The interpretation of secondary outcomes is also constrained by the timeframes and assessment procedures. The primary and several listed event outcomes concern a short treatment period, while concentration of trough anti-IIa activity is measured over treatment and follow-up. Those different endpoints answer different questions. Secondary findings can provide context, but they do not replace the primary analysis, resolve the discrepancy between sponsor and recalculated results, or establish a broader treatment effect.

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

• Percentage of Participants With Proximal DVT Over 10 ± 2 Days of Treatment
• Percentage of Participants With Distal DVT Over 10 ± 2 Days of Treatment
• Percentage of Participants With PE Over 10 ± 2 Days of Treatment
• Number of Death Due to VTE Over 10 ± 2 Days of Treatment
• Percentage of Participants With Total Asymptomatic VTE Over 10 ± 2 Days of Treatment
• Percentage of Total Symptomatic VTE Over 10 ± 2 Days of Treatment
• Concentration of Trough Anti-IIa Activity Over the Duration of Treatment and Follow-up
• Percentage of Participants With Major Bleeds Over 10 ± 2 Days of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What is the primary result? The endpoint is a binary event outcome: each participant either met the total VTE definition or did not. A percentage is a way to express the share of the analyzed group with the event. Its interpretation depends on the event definition, the participants included in the denominator, and how missing or unevaluable assessments were handled. The registry gives an ITT population description beginning with randomized participants who received at least one dose, but the remainder of the denominator description is cut off. Further operational detail is not reported in the registry record.

What does a confidence interval express? A confidence interval communicates the statistical precision of an estimate under the method used to calculate it. For each posted group percentage, the 95% confidence interval gives a range of values compatible with the observed data under that procedure. A wider interval indicates less precision than a narrower interval. The interval does not show the probability that a particular treatment is better, and overlap or non-overlap between separate group intervals is not a substitute for a direct comparison.

What is a risk difference? The recalculated comparisons express the difference between two event percentages on the absolute scale. A value below zero means the event percentage in the comparison group is lower than in the reference group under the stated subtraction direction; a value above zero means it is higher. A value of zero corresponds to no absolute difference. The recalculated confidence intervals and p-values use unadjusted comparisons from the posted summary statistics. They are not a replacement for the sponsor’s own analyses, particularly because the record flags a discrepancy.

How does a p-value fit in? A p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions are appropriate. It is not the probability that the null hypothesis is true, nor a direct measure of the size or importance of a difference. A p-value should be considered alongside the estimate and its interval. In this trial, the recalculated p-values are unadjusted; the registry does not report whether or how the sponsor’s analyses accounted for multiple comparisons.

Why distinguish risk ratios from risk differences? A risk ratio compares event probabilities as a relative measure, whereas a risk difference compares them as an absolute measure. The sponsor-reported primary analyses are identified as risk ratios from Fisher Exact methods. The simple recalculations are risk differences. These measures answer related but non-identical questions and have different scales, so their estimates cannot be compared as if they were the same statistic. The registry does not report enough detail to reconcile all differences between the sponsor results and recalculations. Given the recorded discrepancy, the sponsor analysis takes precedence.

What does Fisher Exact mean? In general, Fisher’s exact test is a method for evaluating association in a two-group binary-outcome comparison using the observed counts. It does not require the large-sample approximation used by some other procedures. Its reported p-value still depends on the defined comparison and analysis choices. The registry names Fisher Exact for the sponsor’s risk-ratio analyses, but a fuller account of the test implementation, sidedness, and any adjustment is not reported in the registry record.

What is the role of adjudication? In general, independent event adjudication applies prespecified criteria to determine whether reported events meet the outcome definition. The primary endpoint description names an Independent Central Adjudication Committee. This can help make outcome classification more consistent, but it cannot eliminate incomplete detection or make different types of events identical. Here the composite includes symptomatic events, imaging-detected asymptomatic DVT, and VTE-related death, while venography was not mandatory for all asymptomatic participants completing the study.

What does the registered design tell readers? The registry labels the trial randomized and double-masked, yet its model field says single group and the results list four treatment groups. Those fields do not form a fully coherent description. The record does not clarify the discrepancy. The group-level results support describing comparisons among the listed groups, but they do not reveal the full operational design or allocation process. Randomization methods, masking details, and allocation ratio are not reported in the registry record.

Why are planning figures not evidence about the trial’s power? The sample-size figures are illustrations derived from observed effects under stated assumptions, not the original trial’s sample-size plan. They show how a hypothetical future comparison’s required group size changes as the effect targeted for detection changes. Planning calculations depend on their assumptions and should not be used to infer what the trial was designed to detect. The original design justification and original assumptions are not reported in the registry record.

Why can over-dispersion matter in general? For outcomes that vary more than a chosen statistical model expects, over-dispersion can make standard errors too small and confidence intervals too narrow if it is ignored. This is a general concern for some count and rate outcomes. The primary endpoint is a binary percentage, and the registry does not report an over-dispersion analysis for it. This general concept should not be mistaken for a reported feature of this trial.

11. Confidence Intervals and Precision

The primary group percentages have 95% confidence intervals that communicate uncertainty in the estimated event percentages. For Odiparcil MR 250 mg Tablet, the estimate is 45.1% with a 95% confidence interval of 37.4 to 53.1. For Odiparcil MR 375 mg Tablet, it is 44.4% with an interval of 36.8 to 52.2. For Odiparcil MR 500 mg Tablet, it is 41.3% with an interval of 33.5 to 49.3. For Warfarin INR 2.0 to 3.0, it is 31.2% with an interval of 24.1 to 39.1.

These intervals are not especially narrow: each spans a range of values around its point estimate. That means the group percentages are estimated with meaningful uncertainty. The comparison intervals are also important. For the recalculated risk difference between 375 mg and the 250 mg reference, the interval extends from -0.114 to 0.099. For 500 mg versus the reference, it extends from -0.146 to 0.069. Both intervals include zero and values on either side of zero, so the recalculations are compatible with more than one direction of difference.

For the recalculated warfarin comparison, the interval extends from -0.244 to -0.034. While this interval does not include zero, that finding belongs to the unadjusted recalculation and must be considered alongside the discrepancy with sponsor-reported analyses. The posted sponsor analyses use risk ratios rather than risk differences, and one reported group pairing appears twice with differing results. The record does not explain the difference.

In general, interval width depends on factors such as the amount of information and the variability of the outcome. The posted intervals describe uncertainty under their respective methods; they do not account automatically for every design limitation, missing outcome, or multiplicity concern. The registry record does not report a complete account of missing data or a multiplicity adjustment, so the intervals should not be taken as resolving those issues.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the original sample-size justification for this trial. The assumptions stated for the illustration 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 at the stated fraction of the observed effect. The figures for these binary outcomes are participants per arm, not total events.

In general, 80% power means that if the assumed effect and other planning assumptions were correct, a hypothetical study of the specified size would have an 80% chance of rejecting the null hypothesis using the stated test procedure. The 90% column expresses the same planning idea with a higher target chance of detecting the assumed effect. A higher target power generally requires a larger planned sample under otherwise unchanged assumptions.

The rows describe planning for 100%, 75%, or 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so planning to detect a smaller effect requires more participants. The resulting figures can change sharply across those assumptions, and they should be interpreted as illustrations rather than forecasts for a particular future study. The original design assumptions, including the trial’s own intended effect and sample-size justification, are not reported in the registry record.

These figures are not observed power. Observed power calculated from an effect estimate after the trial would largely restate the observed result and is not a measure of how precise that result is. The confidence intervals around the actual estimates are more useful for understanding the uncertainty in the posted outcomes. The registry’s sample-size assumptions apply to these planning illustrations only; no time-to-event planning result is described for this primary binary endpoint.

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 = 0.451; treatment proportion p₁ = 0.444; average p̄ = 0.448.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7032 = 1.3782.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7032 = 0.5918.
4. n = (1.3782 + 0.5918)² / (-0.0074)² = 70,255.9, rounded up to 70,256 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 <- 0.451219512195122                          # control proportion
p1 <- 0.443786982248521                          # 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(244725)
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 = 70,256 (80% power), 94,053 (90% power)
 75% of observed effect: n per arm = 124,950 (80% power), 167,272 (90% power)
 50% of observed effect: n per arm = 281,246 (80% power), 376,507 (90% power)
power.prop.test: 70255.9 
Simulated power at n = 70,256 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry lists sponsor-reported analyses for risk ratios using Fisher Exact methods. For Odiparcil MR 250 mg Tablet versus Warfarin INR 2.0 to 3.0, one entry reports a risk ratio of 1.45, 95% confidence interval 1.1 to 1.9, and p = 0.012. For Odiparcil MR 375 mg Tablet versus warfarin, it reports a risk ratio of 1.42, 95% confidence interval 1.1 to 1.9, and p = 0.017. A further entry for the 250 mg and warfarin groups reports a risk ratio of 1.32, 95% confidence interval 1.0 to 1.8, and p = 0.080.

The recalculated comparisons use unadjusted risk differences, calculated from the posted summary statistics. Those are different effect measures and are not interchangeable with the sponsor’s risk ratios. In addition, the discrepancy flag indicates that the recalculated results do not fully agree with the sponsor’s reported analysis. The sponsor’s own analysis takes precedence over the simple recalculations for describing the trial’s reported inferential results.

The registry gives two differing sponsor-reported results for the same stated 250 mg-versus-warfarin group pairing, but does not explain why both are present. That ambiguity should remain visible in interpretation. The recalculations are useful as a transparent, unadjusted check on the posted summary data; they should not be presented as a correction to or replacement for the sponsor’s analysis. Details that could reconcile the results, such as the full analysis plan and exact analysis populations, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The record identifies a primary endpoint and 11 posted secondary outcomes, with several potential treatment-group comparisons. When many outcomes or comparisons are evaluated, the chance of obtaining at least one apparently strong result by chance can increase. Statistical methods can address this through a prespecified testing hierarchy, adjustment of significance thresholds, or other strategies. The registry record does not report whether such a strategy was planned or used, so the posted p-values should be read as reported rather than assumed to be adjusted for multiplicity.

The sponsor-reported analyses include more than one result for the same stated 250 mg and warfarin group pairing, with differing risk ratios and p-values. The registry does not explain whether those entries reflect different analysis populations, analysis methods, or a reporting issue. That ambiguity complicates a simple account of which result represents the intended comparison. It is separate from the issue of multiplicity and should not be interpreted as evidence of a particular explanation.

The primary population description states that the ITT population comprised participants randomized and given at least one dose, but the registry text ends before completing its description of which participants and venograms were used for analysis. The outcome description also notes that venography was not mandatory for every asymptomatic participant at study completion. The exact handling of missing, absent, or unevaluable venograms and other missing primary outcome data is not reported in the registry record. Nor are sensitivity analyses for missing data described.

In general, missing outcome data can affect both the estimated percentage and the validity of comparisons if the likelihood of being observed is related to treatment or outcome status. The direction and extent of any such effect cannot be inferred from the registry summary. The full statistical analysis plan, prespecified analysis hierarchy, and details of protocol deviations are not reported. Accordingly, the posted results support a description of the available registry findings but do not allow a complete audit of the analysis choices.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: wound dehiscence (0.8%), atrial fibrillation (0.8%), pneumonia (0.4%), postoperative wound infection (0.4%), bronchitis acute (0.4%).

The registry lists serious adverse events by treatment group. The reported group figures are 14 affected participants among 235 at risk for Odiparcil MR 250 mg Tablet, 11 among 243 for Odiparcil MR 375 MG TABLET, 16 among 239 for Odiparcil MR 500 MG TABLET, and 9 among 237 for WARFARIN INR 2.0 TO 3.0. These are serious adverse event counts and denominators as recorded; they should not be confused with the primary VTE endpoint denominators or interpreted as adjusted comparisons.

The listed serious adverse event terms and percentages include Wound dehiscence at 0.8%, Atrial fibrillation at 0.8%, Pneumonia at 0.4%, Postoperative wound infection at 0.4%, Bronchitis acute at 0.4%, and Viral upper respiratory tract infection at 0.4%. These entries describe the terms reported as most frequent among serious adverse events; they do not provide a complete account of every event or its relationship to treatment.

Deaths are not reported in the registry record’s adverse event summary. No causal attribution, comparative safety analysis, or detailed event-level account can be established from these figures alone. The registry also lists counts of participants with other adverse events, but those counts should be read separately from serious adverse events. Interpretation is limited because the record does not provide full definitions, exposure-adjusted analyses, or detail on missing safety information.

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

The registry record documents event percentages for four listed treatment groups during a short period after total knee replacement. The primary endpoint is a composite total VTE outcome, and the group estimates have confidence intervals that show appreciable uncertainty. The recalculated comparisons between the two higher-dose odiparcil groups and the 250 mg reference group have intervals spanning no difference. The recalculated warfarin comparison has an interval that does not span no difference, but the record flags a discrepancy with sponsor-reported results. Those sponsor analyses should take precedence over the simple recalculations when describing the trial’s own inferential findings.

The result does not by itself prove that any treatment is effective or ineffective. It does not establish equivalence among groups, because absence of a clear difference is not the same as evidence that outcomes are sufficiently similar. It also does not establish a treatment effect beyond the recorded population, endpoint definition, and follow-up period. The primary endpoint combines symptomatic events, imaging-detected asymptomatic DVT, and VTE-related death; it is not a direct measure of every aspect of patient experience or disease severity.

The available record does not fully describe the primary analysis population, missing outcome handling, multiplicity strategy, sample-size justification, or complete statistical analysis plan. It also contains a mismatch between its randomized classification, single-group model field, and multiple reported groups, as well as an unexplained repeated sponsor comparison with differing values. These gaps limit independent reconstruction of the analysis.

Safety counts provide a separate descriptive view and cannot be reduced to the primary endpoint result. The listed serious adverse events and other adverse events do not, on their own, establish comparative safety. The findings should therefore be understood as registry-reported results with specific design and reporting limitations, rather than as a complete evaluation of clinical benefit and risk.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition must be read closely before interpreting a percentage. The total VTE outcome combines symptomatic events, asymptomatic DVT identified through assessment, and VTE-related death. Because the registry says venography was not mandatory for every asymptomatic participant completing the study, the recorded composite depends partly on ascertainment procedures, not only on whether a biological event occurred.

It also illustrates the distinction between a group event percentage and a comparative effect estimate. The arm-level percentages describe observed event frequencies, while risk differences and risk ratios express contrasts on different scales. A comparison should be interpreted with its uncertainty interval, not just its point estimate or p-value. The recalculations and sponsor results do not fully align, making it important to identify which analysis is being described and to avoid presenting a recalculation as the trial’s definitive analysis.

The record’s internal inconsistencies are statistically relevant. Its randomized and double-masked classification coexists with a single-group model label and multiple treatment groups. The sponsor analysis lists a repeated group pairing with differing results. These details affect how confidently an independent reader can reconstruct design and inference.

Finally, the planning illustrations show how design targets depend on assumptions about the effect to detect and desired power. They are not evidence that the completed trial had a particular observed power or that its original design used those assumptions. The trial is therefore useful for teaching interpretation of composite outcomes, uncertainty, analysis discrepancies, and the distinction between actual results and planning calculations.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations arise from the registry description. The primary outcome uses a composite that includes symptomatic DVT or PE, asymptomatic DVT detected through venography, and death adjudicated as related to VTE. These components may differ in clinical significance and ascertainment. The composite percentage does not show the contribution of each component, and the registry states that mandatory venography was not required for every asymptomatic participant at study completion.

The registry identifies the study as randomized and double-masked but labels its model single group, while listing four treatment groups with primary results. The record does not explain this metadata inconsistency. It also does not report randomization procedures, allocation ratio, masking details, or the original sample-size justification. The enrollment figure and primary-outcome group denominators are not reconciled in the record, and group counts should not be combined to infer an analysis population.

The primary population description is incomplete, and handling of missing or unevaluable outcome assessments is not reported. The registry does not provide the complete statistical analysis plan, multiplicity strategy, or sensitivity analyses. A discrepancy is flagged between sponsor-reported and unadjusted recalculated comparisons, and sponsor entries include a repeated group pairing with differing estimates. The reason for this is not reported.

Follow-up for the primary endpoint is limited to the stated treatment period. Longer-term outcomes are not reported in the primary result. The safety summary is also limited: it provides group counts and selected serious adverse event terms, but not a complete event-level assessment, causal attribution, or a detailed comparative analysis. These reporting gaps limit the strength and scope of conclusions that can be drawn from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Odiparcil For The Prevention Of Venous Thromboembolism — NCT00244725.
• Registry record last updated 2017-05-02; status last verified 2017-03.
• Results first posted 2017-05-02.
• 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

NCT00244725 is a completed Phase 2 trial sponsored by GlaxoSmithKline, with a recorded start of 2005-09 and primary completion of 2006-09. The registry describes the study as randomized and double-masked, lists an enrollment of 961, and gives results for three odiparcil regimens and warfarin after total knee replacement.

The primary outcome was the percentage of participants with total VTE over 10 ± 2 days of treatment. Posted group percentages range from 31.2% for Warfarin INR 2.0 to 3.0 to 45.1% for Odiparcil MR 250 mg Tablet, with group confidence intervals reflecting uncertainty. Sponsor-reported risk-ratio analyses and unadjusted recalculated risk differences are not fully aligned; the sponsor analysis takes precedence, and an unexplained repeated sponsor comparison remains a reporting ambiguity.

The registry’s single-group model label does not align clearly with its randomized classification and multiple reported groups. Details on the original sample-size justification, complete analysis population, missing data, and multiplicity are not reported in the registry record. Safety findings are descriptive and should be interpreted separately from the primary VTE result.