A Study to Evaluate the Efficacy and Safety of Fondaparinux for the Prevention of Venous Blood Clots in Patients With a Plaster Cast or Other Type of Immobilization for a Below-knee Injury Not Needing Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of Fondaparinux for the Prevention of Venous Blood Clots in Patients With a Plaster Cast or Other Type of Immobilization for a Below-knee Injury Not Needing Surgery (NCT00843492), a randomized phase 3 study. The primary outcome is Number of Participants With Venous Thromboembolism (VTE) or Death up to the Time of Complete Mobilization.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group, open-label study sponsored by GlaxoSmithKline. The registry lists an enrollment of 1351. The study is marked completed. Its recorded start is 2008-12, and its primary completion is 2010-01. The official title describes a multicentre comparison of fondaparinux with low molecular weight heparin (nadroparin) in patients needing rigid or semi-rigid immobilization after an isolated non-surgical below-knee injury.

Participants were assigned to fondaparinux or nadroparin. The study had no masking, so the registry identifies it as open-label. The planned treatment period extended from randomization until complete mobilization, corresponding to cast or brace removal, subject to a minimum of 21 days and a maximum of 45 days. The fondaparinux description includes a lower dose for patients with creatinine clearance between 30 and 50 mL/min. The nadroparin description gives its daily dose as 2850 anti-Xa IU (0.3 mL).

The primary endpoint was assessed from Day 1 to complete mobilization plus 2 days; the registry reports an average of 35.9 study days for this timeframe. The primary analysis counts were 48 of 586 for nadroparin and 15 of 584 for fondaparinux. Those analysis denominators should not be treated as interchangeable with the overall enrollment figure. The record does not explain the difference between enrollment and the endpoint-analysis counts.

The registry lists six secondary outcomes, including further VTE and death outcomes, bleeding outcomes, and bleeding assessed by the Central Adjudication Committee. Detailed participant counts and a recalculated comparison are posted for the confirmed VTE and death outcome through final visit or contact. Results for the other listed secondary outcomes are not reported in the registry record. The original sample-size justification, allocation procedure details, and full statistical analysis plan 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all randomized participants with a VTE status or experiencing death. Participants without evaluation of the primary endpoint in the timeframe requested by the protocol were considered as missing data and therefore not included in the primary efficacy 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 Number of Participants With Venous Thromboembolism (VTE) or Death up to the Time of Complete Mobilization, measured over Day 1 to complete mobilization plus 2 days (average of 35.9 study days).

The primary endpoint counts participants with venous thromboembolism or death up to complete mobilization, assessed through complete mobilization plus 2 days. The registry defines VTE to include asymptomatic DVT found by systematic compression ultrasonography, symptomatic DVT, and symptomatic fatal or non-fatal pulmonary embolism. The outcome also includes death. Events and deaths were adjudicated by the independent Central Adjudication Committee.

This composite brings together events that differ in how they are detected and in their clinical presentation. Systematic ultrasound can identify DVT without symptoms, while the other VTE components are symptomatic. Death is included as a separate component. A participant is counted as having the endpoint if an eligible component is recorded within the specified timeframe; the posted participant counts do not show how many events of each component occurred separately. Component-specific primary-endpoint counts are not reported in the registry record.

The endpoint is useful for comparing the recorded occurrence of thromboembolic events or death during the period of immobilization and shortly after complete mobilization. Its interpretation depends on the stated timeframe and on how missing endpoint evaluations were handled. The registry says that participants without evaluation of the primary endpoint in the protocol timeframe were considered missing and were not included in the primary efficacy analysis. Consequently, the primary result describes the analyzed participants with endpoint information under that definition; it does not by itself describe what happened to participants whose endpoint status was missing.

7. Results Posted in the Registry

• Fondaparinux: 2.6% (15/584) versus 8.2% (48/586) on control; risk difference -5.6 percentage points (95% CI -8.2 to -3.1), risk ratio 0.31 (0.18–0.55); 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 Confirmed VTE and Death up to the Final Visit or Contact

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fondaparinux: 2.4% (15/621) versus 7.9% (49/622) on control; risk difference -5.5 percentage points (95% CI -7.9 to -3.0), risk ratio 0.31 (0.17–0.54); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Fondaparinux than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists six secondary outcomes, spanning VTE and death, different follow-up windows, and bleeding categories. Detailed counts and a recalculated comparison are posted for confirmed VTE and death through final visit or contact. That result is directionally consistent with the primary endpoint comparison, but it uses a longer follow-up definition than the primary outcome. The remaining listed secondary outcomes do not have detailed results in the registry record.

Secondary outcomes can help describe whether the primary pattern is accompanied by findings on related outcomes, including later VTE and safety measures. They do not replace the primary endpoint, which was the designated main efficacy outcome in the registry. The confirmed VTE and death outcome overlaps conceptually with the primary composite but is not identical in its time window. The record does not provide component-level results that would establish which events contributed to either endpoint.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of at least one apparently notable result can increase as the number of tests grows. This is a general statistical concern, not a claim about how the sponsor analyzed the trial. A multiplicity adjustment or a prespecified hierarchy can address this issue, but whether such procedures were specified or used is not reported in the registry record. Without those details, the secondary results are best treated as supportive or exploratory rather than as separate confirmatory evidence.

The listed secondary bleeding outcomes are relevant to interpreting the study’s safety reporting, but the posted adverse-event counts are not a substitute for outcome-specific trial comparisons. The record’s incomplete secondary-result detail also limits any attempt to describe a comprehensive overall pattern across all listed outcomes. The available secondary comparison is consistent in direction with the primary result, while the rest cannot be characterized from the posted results.

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

• Number of Participants With Any Adjudicated Components of VTE, Asymptomatic DVT, Symptomatic DVT, Symptomatic PE, and Death
• Number of Participants With Confirmed VTE and Death up to the Final Visit or Contact
• Number of Participants With Major Bleeding From Day 1 to Complete Mobilization and From Day 1 up to the Final Visit or Contact
• Number of Participants With Clinically Relevant Non-major Bleeding From Day 1 to Complete Mobilization and From Day 1 up to the Final Visit or Contact
• Number of Participants With Minor Bleeding From Day 1 to Complete Mobilization and From Day 1 up to the Final Visit or Contact
• Participants With Any Incidence of Any Bleeding Event as Adjudicated by a CAC) From Day 1 to Complete Mobilization and From Day 1 up to the Final Visit or Contact

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a binary primary outcome: whether a participant had VTE or death in the defined timeframe. For a binary outcome, the group count is the number of participants with the event, and the denominator is the number included in that group’s analysis. The primary counts are 48 of 586 for nadroparin and 15 of 584 for fondaparinux. A comparison can be expressed in different ways, including a risk difference or an odds ratio. Each expresses the group contrast on a different scale, so their numerical values are not directly interchangeable.

What does the risk difference express?

The recalculated risk difference subtracts the recorded event proportion in the nadroparin group from that in the fondaparinux group. The estimate is -0.056. A negative value means that the observed proportion was lower in the fondaparinux group for this coding of the comparison. Its 95% confidence interval runs from -0.082 to -0.031. Since the interval lies below zero, it is compatible with a difference favoring fondaparinux on this measure. This is an unadjusted recalculation from the posted summary counts, not a substitute for the sponsor’s reported analysis.

What does an odds ratio express?

An odds ratio compares the odds of the endpoint between groups rather than subtracting event proportions. The sponsor reports an odds ratio of 0.30, with a 95% confidence interval from 0.15 to 0.54. Values below 1 indicate lower odds in the fondaparinux group relative to nadroparin for this comparison. An odds ratio is not the same as a risk difference, and it should not be read as an absolute change in the number of participants with the outcome. The registry does not report an adjusted odds ratio in the posted analysis summary.

What does the p-value say?

The sponsor’s reported p-value is <0.001; the unadjusted recalculation also gives p < 0.001. A p-value describes how unusual data at least this discordant with a specified no-difference model would be if that model and the analysis assumptions held. It does not give the probability that either treatment is effective, nor does it measure the size or importance of the difference. The p-value is also not a measure of precision by itself; the confidence interval gives more direct information about the range of estimates compatible with the data under the method used.

Why does the timeframe matter?

The primary outcome covers Day 1 through complete mobilization plus 2 days, with an average of 35.9 study days. It combines asymptomatic DVT detected through systematic ultrasound, symptomatic DVT, symptomatic fatal or non-fatal pulmonary embolism, and death. The composite can be informative as a count of participants with any qualifying outcome, but it cannot reveal the separate contribution of each component when only the combined total is posted. The registry says that an independent Central Adjudication Committee adjudicated events and deaths. Details of the adjudication process are not reported in the registry record.

What does the randomized design contribute?

Random allocation is intended to support a fair comparison between assigned groups by reducing systematic differences in treatment assignment. The registry identifies the study as randomized and parallel, but the method used to generate or conceal the allocation is not reported in the registry record. The study was open-label, so participants and study staff were not masked to group assignment according to the registry’s masking designation. Independent adjudication is reported, but the record does not say whether adjudicators were masked.

The primary population is described as randomized participants with VTE status or death. Participants without a primary-endpoint evaluation in the protocol timeframe were treated as missing and not included in the primary efficacy analysis. This is not the same as counting every randomized participant regardless of endpoint availability. The registry does not report the number with missing primary endpoint data, the reasons for missingness, or sensitivity analyses addressing it. Those details matter because excluding participants with unknown outcomes can affect interpretation if missingness is related to group or outcome.

Why can over-dispersion matter in other endpoint types?

General explanation: for count outcomes, a statistical model may assume that the variability is described by a particular distribution. Over-dispersion means the observed variability is greater than that assumption allows. If ignored, standard errors can be too small and confidence intervals too narrow. The primary outcome in this trial is posted as participants with an event, not a repeated-event count, and the registry does not report a model for over-dispersion. This concept therefore does not change the interpretation of the reported binary endpoint.

The registry reports the sponsor’s primary analysis as a Fisher Exact analysis of an odds ratio. Fisher’s exact test is a method for comparing categorical outcomes using the observed group counts. The record does not provide a fuller statistical analysis plan, details on any prespecified covariate adjustment, or interim-analysis information; those items are not reported in the registry record. The recalculated risk difference and its interval are simple unadjusted calculations from the posted summary statistics and should be read alongside, not in place of, the sponsor’s reported analysis.

11. Confidence Intervals and Precision

The sponsor’s odds-ratio estimate is 0.30, with a 95% confidence interval from 0.15 to 0.54. The interval excludes 1, the value corresponding to equal odds between groups, and its endpoints are on the side of the estimate that indicates lower odds for fondaparinux. It nevertheless covers a range of possible relative effects; the estimate should not be treated as an exact value.

The unadjusted risk-difference recalculation is -0.056, with a 95% confidence interval from -0.082 to -0.031. The interval excludes zero, the no-difference value for this measure. Its negative endpoints indicate that the estimated difference is in the direction of a lower recorded event proportion in the fondaparinux group. The interval communicates uncertainty around the recalculated group contrast, given the method used and the posted counts.

A confidence interval is not a range that contains the true effect with a fixed probability after the data have been observed. In general, a 95% confidence interval describes a procedure that would cover the underlying parameter in 95% of repeated samples if its assumptions held. It is useful for assessing both the direction and precision of an estimate, but it does not address all sources of uncertainty, such as missing endpoint data, outcome ascertainment, or limits in generalizability.

The secondary recalculation has a risk difference of -0.055, with a 95% confidence interval from -0.079 to -0.030. This interval also excludes zero and is in the same direction as the primary recalculation. It concerns a different outcome window, extending to final visit or contact, so it should not be treated as a duplicate measurement of the primary endpoint. The registry does not report confidence intervals for all listed secondary outcomes.

Precision depends on the number of observed outcomes as well as the analysis method and group sizes. The confidence intervals are relatively informative about the direction in these posted comparisons, but they cannot make the result certain or remove limitations in how the endpoint and analysis population were defined.

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 figures are planning illustrations based on the observed primary effect, not the trial’s original design calculation. The registry record does not report the assumptions used for the trial’s original sample-size justification. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show the participants per arm for 80% power and participants per arm for 90% power when planning for 100%, 75%, or 50% of the observed effect.

For planning for 100% of the observed effect, the illustration gives 252 participants per arm for 80% power and 337 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 504 participants per arm for 80% power and 674 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 1,256 participants per arm for 80% power and 1,680 participants per arm for 90% power. These are per-arm participant counts, not total events.

In plain terms, 80% power is the planned chance of detecting an effect of the specified size at the stated significance level if that effect is the true one and the assumptions hold. The 90% power column describes a higher target chance under the same general planning framework. For either target, planning for a smaller effect requires more participants: the effect assumed at 75% or 50% of the observed effect is smaller than the full observed effect, and the illustrated participant requirements are larger.

These figures are not observed power. They are prospective illustrations calculated from the observed effect and should not be used as evidence that the trial was adequately designed or that its result is likely to replicate. The original design assumptions are not reported in the registry record.

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 = 0.082; treatment proportion p₁ = 0.026; average p̄ = 0.054.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3191 = 0.6254.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3166 = 0.2664.
4. n = (0.6254 + 0.2664)² / (-0.0562)² = 251.6, rounded up to 252 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 <- 0.0819112627986348                          # control proportion
p1 <- 0.0256849315068493                          # 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(843492)
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 = 252 (80% power), 337 (90% power)
 75% of observed effect: n per arm = 504 (80% power), 674 (90% power)
 50% of observed effect: n per arm = 1,256 (80% power), 1,680 (90% power)
power.prop.test: 251.6 
Simulated power at n = 252 per arm: 0.819 (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 own primary analysis is reported as a Fisher Exact analysis of an odds ratio. It gives an odds ratio of 0.30, a 95% confidence interval from 0.15 to 0.54, and p < 0.001. This analysis uses the odds-ratio scale and is the registry’s reported analysis for the primary outcome.

The recalculated result uses the posted participant counts to estimate an unadjusted risk difference of -0.056, with a 95% confidence interval from -0.082 to -0.031 and p < 0.001. It is a straightforward re-analysis of summary counts, not a reconstruction of any additional sponsor methods that are not reported. The odds ratio and risk difference answer related but different statistical questions: one compares odds, while the other expresses an absolute difference in event proportions.

The two analyses agree in direction and both report a p-value below 0.001. The registry record does not flag a discrepancy between the sponsor result and the recalculation. The sponsor’s reported analysis takes precedence as the trial’s own analysis; the recalculation is supplementary and should not be presented as if it were the sponsor’s prespecified method.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical conclusions are drawn from several outcomes or comparisons. Each additional test creates another opportunity for a result to appear statistically notable by chance, even if no underlying difference exists. This trial registry lists six secondary outcomes in addition to the primary endpoint. Whether the protocol used a prespecified hierarchy, adjusted the significance threshold, or controlled a family-wise error rate is not reported in the registry record. The primary result should therefore be distinguished from unadjusted secondary findings, which warrant more cautious interpretation when multiplicity handling is unknown.

The registry’s sponsor analysis reports a Fisher Exact analysis for the primary endpoint, and the posted secondary comparison is an unadjusted recalculation from summary counts. The record does not report interim analyses, stopping rules, or a complete statistical analysis plan. Their absence from the record does not establish whether they were used; it means those details are not reported in the registry record.

For the primary efficacy population, the registry states that randomized participants with VTE status or who experienced death were included. Participants without an evaluation of the primary endpoint in the requested protocol timeframe were considered to have missing data and were not included in the primary efficacy analysis. The record does not give the number of participants with missing endpoint evaluations, reasons for missingness, or results from sensitivity analyses. It also does not describe an imputation method. These omissions make it difficult to assess how robust the primary comparison is to alternative assumptions about missing outcomes.

The primary analysis denominators are 586 for nadroparin and 584 for fondaparinux, while overall enrollment is recorded as 1351. The registry does not explain the difference between these figures, so no cause should be inferred. Differences in analysis populations or endpoint availability may be relevant, but the record does not give enough detail to determine why the primary denominators differ from overall enrollment. The stated analysis-population definition and missing-data handling should therefore remain part of any interpretation of the result.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: haematoma infection (0.1%), subcutaneous abscess (0.1%), joint dislocation (0.1%), ankle fracture (0.1%), faecaloma (0.1%).

The registry reports serious adverse events for 9 of 670 participants in the nadroparin group and 6 of 674 in the fondaparinux group. It also reports other adverse events for 95 of 670 and 93 of 674, respectively. These are descriptive group counts as posted in the safety record; they are not the primary efficacy endpoint and are not presented as an adjusted comparison.

The listed serious-event terms include haematoma infection, subcutaneous abscess, joint dislocation, ankle fracture, faecaloma, and fracture malunion, each recorded as 0.1%. The registry does not give additional detail for these terms in the registry entries, such as event timing, seriousness criteria, or a treatment-relatedness assessment. The record does not report deaths in the safety summary.

Safety counts should be read with their stated denominators and outcome definitions. They do not show whether an event was caused by the assigned drug, and a simple comparison of counts does not establish a difference in safety. The registry’s listed serious-event terms are descriptive, and the absence of a term from that list should not be taken to mean that it did not occur.

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

The registry’s primary result shows fewer participants recorded with VTE or death in the fondaparinux group than in the nadroparin group during the stated period from Day 1 to complete mobilization plus 2 days. The sponsor-reported odds ratio and the unadjusted risk-difference recalculation point in the same direction, and both report p < 0.001. This is evidence of a statistical difference in the posted trial outcome under the analyses described.

The result does not, by itself, establish the effect for every patient with a lower-leg injury, for immobilization strategies outside the study criteria, or for follow-up beyond the registry’s stated endpoint windows. The trial population was restricted to patients with an isolated non-surgical below-knee injury requiring rigid or semi-rigid immobilization. The primary result includes both asymptomatic DVT detected by systematic ultrasound and symptomatic events, along with death. The posted total does not distinguish the contribution of each component.

A statistically significant result is not the same as a measure of clinical importance. Interpretation of importance depends on the outcome, the magnitude and precision of the difference, and the context in which treatment is used. The registry’s counts and confidence intervals characterize the comparison but do not answer every question about the balance of benefits and harms. Safety counts are descriptive, and the record does not provide a comprehensive treatment-attribution analysis.

The result also does not remove uncertainty related to missing endpoint information. The primary efficacy analysis excluded participants who lacked evaluation in the protocol timeframe, and the number and reasons for missing outcomes are not reported in the registry record. Open-label assignment and the absence of reported details on allocation procedures and adjudication masking are further considerations. An independent committee adjudicated VTE events and deaths, but the record does not specify its procedures.

Accordingly, the posted findings support a difference in the recorded primary endpoint between the randomized groups in this study. They should be interpreted within the trial’s eligibility criteria, endpoint definition, follow-up, analysis population, and reporting limitations rather than as a general treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates how a registry result depends on a clearly defined endpoint and time window. The primary outcome is not simply a count of symptomatic clots: it includes asymptomatic DVT detected by systematic compression ultrasonography, symptomatic DVT, pulmonary embolism, and death. That composite definition affects what the group comparison means, and the absence of component-specific primary counts limits further interpretation.

It also shows why the reported analysis and a simple recalculation should be distinguished. The sponsor reports an odds ratio from a Fisher Exact analysis, while the recalculation expresses the same posted counts as an unadjusted risk difference. The two measures agree on the direction of the comparison but communicate different quantities. Keeping the methods and scales explicit prevents treating unlike estimates as interchangeable.

The record is also a reminder that endpoint availability shapes the analysis population. The primary efficacy analysis excludes participants without an evaluation in the protocol timeframe, but the missing count and sensitivity analyses are not reported. These details matter because a precise-looking estimate cannot resolve uncertainty about participants whose outcomes are unknown.

Finally, the study’s multiple listed secondary outcomes raise a familiar issue in clinical research: results across many outcomes need context about prespecification and multiplicity. The registry does not report that information. Separating the primary result from secondary findings, and separating descriptive safety counts from comparative efficacy estimates, supports a more disciplined reading of the evidence.

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 primary endpoint is a composite. It combines asymptomatic DVT detected by systematic ultrasound, symptomatic DVT, symptomatic pulmonary embolism, and death. The registry does not post separate primary counts for these components, so the overall group comparison cannot show which component accounts for the observed difference. The primary timeframe ends at complete mobilization plus 2 days, and the reported average is 35.9 study days; the result does not describe a longer-term comparison.

The registry describes the study as open-label. An independent Central Adjudication Committee adjudicated VTE events and deaths, which is relevant to endpoint assessment, but whether adjudicators were masked and how adjudication was conducted are not reported in the registry record. Details of the randomization sequence and allocation concealment are also not reported. These reporting gaps limit assessment of the trial’s safeguards against bias.

The primary efficacy analysis excluded participants without endpoint evaluation in the protocol timeframe. The number of missing evaluations, reasons for missingness, and sensitivity analyses are not reported in the registry record. The record also does not explain why the primary analysis denominators differ from overall enrollment. These points limit assessment of the possible influence of missing outcomes and differences in analysis populations.

The original sample-size justification, interim-analysis procedures, and full statistical analysis plan are not reported in the registry record. Multiplicity handling for the listed secondary outcomes is also not reported. Only one secondary outcome has detailed counts and a recalculated comparison in the posted data, so a complete secondary-outcome pattern cannot be evaluated from the registry record. Safety figures are descriptive and do not establish event causation or provide an adjusted safety comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Fondaparinux for the Prevention of Venous Blood Clots in Patients With a Plaster Cast or Other Type of Immobilization for a Below-knee Injury Not Needing Surgery — NCT00843492.
• Registry record last updated 2016-03-16; status last verified 2014-02.
• Results first posted 2012-07-18.
• 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.

23. Record Summary

The registry record describes a completed phase 3, randomized, parallel-group, open-label study of fondaparinux versus nadroparin in patients requiring immobilization after a non-surgical below-knee injury. Enrollment is listed as 1351. The primary endpoint was VTE or death through complete mobilization plus 2 days, with an average timeframe of 35.9 study days.

The posted primary counts are 48 of 586 for nadroparin and 15 of 584 for fondaparinux. The sponsor reports an odds ratio of 0.30, with a 95% confidence interval from 0.15 to 0.54 and p < 0.001. An unadjusted recalculation gives a risk difference of -0.056, with a 95% confidence interval from -0.082 to -0.031. The record also lists six secondary outcomes, but detailed results are not posted for most of them. Missing primary endpoint evaluations were excluded from the primary efficacy analysis; the number missing and sensitivity analyses are not reported in the registry record.