BIBR 1048 Dose Range Finding Study in Prevention of Venous Thromboembolism in Patients With Primary Elective Total Hip or Knee Replacement Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BIBR 1048 Dose Range Finding Study in Prevention of Venous Thromboembolism in Patients With Primary Elective Total Hip or Knee Replacement Surgery (NCT01225822), a randomized phase 2 study. The primary outcome is Number of Participants With Venous Thromboembolic (VTE) Events.

2. Clinical Question

The primary outcome combined deep vein thrombosis detected by routine bilateral venography with symptomatic DVT confirmed by venography during treatment, or pulmonary embolism confirmed by objective testing. The outcome window extended to the day 8 ± 2 days visit. This question concerns event counts in the analyzed groups; the record does not describe a long-term outcome assessment.

3. Trial Design

The registry describes a randomized, double-masked, parallel-group Phase 2 study, with enrollment of 1973. The trial is listed as completed. The recorded study start was 2002-11, and primary completion was 2003-08. Boehringer Ingelheim is identified as the sponsor.

Participants undergoing primary elective total hip or knee replacement were assigned to one of four BIBR 1048 dose regimens or enoxaparin 40 mg once daily. The BIBR 1048 arms are labeled 50 mg twice daily, 150 mg twice daily, 225 mg twice daily, and 300 mg once daily. The intervention descriptions specify matching placebo capsules and injections to accompany the active treatment, consistent with the registry’s double-masked designation. The 300 mg once-daily arm description itself states BIBR 1048 150 mg once daily, so the record’s arm label and detailed description are not identical.

The primary efficacy outcome was assessed during the treatment period, up to the day 8 ± 2 days visit. Its analysis population was the Full Analysis Set, defined in the registry as randomized patients who had received at least one subcutaneous injection and one oral dose of study medication and had confirmed VTE data after surgery. This is narrower than simply all randomized patients.

The registry lists 11 outcome measures and 36 analyses, while nine secondary outcomes are posted. The original statistical analysis plan, details of randomization procedures, allocation concealment, sample-size justification, and the trial’s planned handling of interim analyses are not reported in the registry record. The posted outcome data therefore support a description of the recorded comparisons, but not a full reconstruction of every protocol decision.

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: Full Analysis Set (FAS) population. This included all randomised patients who had at least one subcutaneous injection and one oral dose of study medication and with confirmed VTE data post surgery

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 Thromboembolic (VTE) Events, measured over Treatment period (up to day 8+/-2 days visit).

The primary endpoint counts participants with venous thromboembolic events during the treatment period. The registry defines events to include proximal or distal deep vein thrombosis detected by routine bilateral venography on day 8 ± 2, symptomatic DVT confirmed by venography during treatment, or pulmonary embolism confirmed by objective testing. The assessment window extended up to the day 8 ± 2 days visit.

This composite combines events detected through scheduled imaging with clinically symptomatic events. Such an endpoint can capture thromboses that might not otherwise become apparent through symptoms alone, while also including clinically recognized DVT and pulmonary embolism. A participant is counted as having an event under the endpoint definition; the posted outcome is a participant count, not an event rate over person-time or a measure of time until an event.

The primary analysis population was the Full Analysis Set. It included randomized patients who received at least one subcutaneous injection and one oral dose of study medication and had confirmed post-surgery VTE data. Consequently, the primary result describes that defined analysis population rather than all people enrolled or all randomized patients. The endpoint is useful for comparing the groups’ recorded VTE counts over the specified treatment window, but it does not by itself describe longer-term recurrence, severity, or outcomes beyond that window.

7. Results Posted in the Registry

• BIBR 1048 150 mg Bid: 13.1% (49/375) versus 23.1% (86/372) on control; risk difference -10.1 percentage points (95% CI -15.5 to -4.6), risk ratio 0.57 (0.41–0.78); unadjusted two-proportion z-test p = <0.001.
• BIBR 1048 225 mg Bid: 10.2% (39/381) versus 23.1% (86/372) on control; risk difference -12.9 percentage points (95% CI -18.1 to -7.6), risk ratio 0.44 (0.31–0.63); unadjusted two-proportion z-test p = <0.001.
• BIBR 1048 300 mg qd: 12.7% (47/371) versus 23.1% (86/372) on control; risk difference -10.4 percentage points (95% CI -15.9 to -5.0), risk ratio 0.55 (0.40–0.76); unadjusted two-proportion z-test p = <0.001.
• Enoxaparin 40 mg qd: 18.8% (72/382) versus 23.1% (86/372) on control; risk difference -4.3 percentage points (95% CI -10.1 to 1.5), risk ratio 0.82 (0.62–1.08); unadjusted two-proportion z-test p = 0.150.

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 VTE Events and All Cause Mortality

• 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:
  • BIBR 1048 150 mg Bid: 13.1% (49/375) versus 23.1% (86/372) on control; risk difference -10.1 percentage points (95% CI -15.5 to -4.6), risk ratio 0.57 (0.41–0.78); unadjusted two-proportion z-test p = <0.001.
  • BIBR 1048 225 mg Bid: 10.2% (39/381) versus 23.1% (86/372) on control; risk difference -12.9 percentage points (95% CI -18.1 to -7.6), risk ratio 0.44 (0.31–0.63); 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 BIBR 1048 150 mg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for BIBR 1048 225 mg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Proximal DVT, PE (Pulmonary Embolism) and VTE Related Mortality

• 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:
  • BIBR 1048 150 mg Bid: 2.9% (11/375) versus 4.0% (15/372) on control; risk difference -1.1 percentage points (95% CI -3.7 to 1.5), risk ratio 0.73 (0.34–1.56); unadjusted two-proportion z-test p = 0.413.
  • BIBR 1048 225 mg Bid: 1.3% (5/381) versus 4.0% (15/372) on control; risk difference -2.7 percentage points (95% CI -5.0 to -0.4), risk ratio 0.33 (0.12–0.89); unadjusted two-proportion z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BIBR 1048 150 mg Bid and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for BIBR 1048 225 mg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Proximal DVT

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • BIBR 1048 150 mg Bid: 2.4% (9/375) versus 4.0% (15/372) on control; risk difference -1.6 percentage points (95% CI -4.2 to 0.9), risk ratio 0.60 (0.26–1.34); unadjusted two-proportion z-test p = 0.206.
  • BIBR 1048 225 mg Bid: 1.3% (5/381) versus 4.0% (15/372) on control; risk difference -2.7 percentage points (95% CI -5.0 to -0.4), risk ratio 0.33 (0.12–0.89); unadjusted two-proportion z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BIBR 1048 150 mg Bid and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for BIBR 1048 225 mg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover additional VTE definitions and components, bleeding outcomes, blood loss and transfusions, laboratory analyses, and dabigatran plasma concentration. The available participant counts show that the endpoint is not limited to the primary composite: some outcomes focus on proximal DVT or combine proximal DVT, pulmonary embolism, and VTE-related mortality. These measures can help describe how the broader outcome pattern relates to the primary endpoint, but they represent distinct definitions and assessment windows.

For the posted VTE-related secondary outcomes, sponsor analyses include logistic-regression comparisons for selected groups. These findings broadly complement the primary endpoint in examining thromboembolic events, but smaller event counts make estimates less precise. A secondary endpoint can also differ from the primary composite because it includes fewer event types or a different time window. It should not be treated as an independent confirmation unless the analysis plan and multiplicity approach support that interpretation.

The registry lists nine posted secondary outcomes, while its outcome-measure listing includes 11 measures and its analysis listing includes 36 analyses. Many outcome comparisons create opportunities for chance findings. Unless multiplicity is controlled or the findings are interpreted as exploratory, unadjusted secondary p-values carry less weight than a prespecified primary analysis. The multiplicity strategy is not reported in the registry record. Secondary outcomes therefore provide context and potential signals, but should be read as a collection of related analyses rather than as separate definitive tests.

Results for bleeding, laboratory measures, blood loss, transfusion, and drug concentration address safety or other aspects of treatment, rather than the primary question of VTE event counts. Their significance depends on their definitions, completeness, and analysis methods. The registry does not report enough detail to infer that every secondary finding was prespecified or to establish a formal hierarchy among them.

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

• Number of Participants With VTE Events and All Cause Mortality
• Number of Participants With Proximal DVT, PE (Pulmonary Embolism) and VTE Related Mortality
• Number of Participants With Proximal DVT
• Volume of Blood Loss
• Rate of Transfusions Due to Bleedings
• Number of Participants With Clinically Significant, Minor or Any Bleeding Events
• Laboratory Analyses
• Plasma Concentration (Cmax) of Dabigatran

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion of participants with an event in one group with the proportion in another. A negative value in these comparisons means that the event proportion in the named group was lower than in the BIBR 1048 50 mg twice-daily reference group, based on the posted counts. Unlike an odds ratio, a risk difference is expressed on the probability scale and can be read as an absolute contrast in event proportions. The recalculated values are simple unadjusted estimates, not the sponsor’s adjusted model estimates.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the data under the statistical method used. It communicates uncertainty around an estimate, rather than indicating that the true value has a particular probability of lying within that specific interval. For a risk difference, an interval that includes zero is compatible with no difference under that calculation; an interval entirely on one side of zero is evidence against zero at the corresponding confidence level, subject to the model and analysis assumptions. Confidence intervals do not account automatically for every source of uncertainty, including multiplicity, missing outcome data, or differences between an unadjusted calculation and an adjusted sponsor model.

Why are the sponsor and recalculated estimates different?

The posted recalculations compare summary counts using unadjusted risk differences, risk ratios, odds ratios, and corresponding intervals and p-values. The sponsor’s recorded primary analyses use logistic regression and report odds ratios. These are different effect measures and can also differ because model-based analyses may use adjustment or analysis details not reflected in a simple comparison of group counts. The covariates and full model specification are not reported in the registry record. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence when describing the trial’s reported inferential findings. Recalculated statistics remain useful as transparent summaries of the posted counts, but they are not a replacement for the trial analysis.

What does a p-value say?

A p-value describes how unusual data at least as incompatible with a stated null model would be if that model and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The recalculated p-values are unadjusted; the registry’s sponsor p-values accompany the logistic-regression analyses. The statistical plan for multiplicity across the many outcome analyses is not reported in the registry record, so isolated p-values should be read cautiously.

Why can event counts be informative yet limited?

Binary outcome counts make the number of participants with and without a recorded event central to interpretation. They allow direct comparison of observed proportions, but provide no information about exactly when events occurred, how long each participant was followed, or the severity of every event. Scheduled venography also means the primary endpoint includes imaging-detected events, not only symptomatic events. The registry does not report a time-to-event primary analysis. A difference in counts should therefore be understood within this endpoint definition and follow-up window, not generalized to outcomes that were not measured.

Why does over-dispersion matter, and is it relevant?

In general, over-dispersion means that observed variability exceeds what a statistical model assumes. It can make standard errors too small if ignored, leading to intervals that are too narrow and p-values that are too optimistic. This concept is most relevant to outcomes modeled as counts or rates when the variance structure is uncertain. The primary outcome is posted as participants with an event, and its recalculated comparisons are binary-outcome comparisons; over-dispersion is not the main concern for those calculations. The registry does not report a complete analysis plan that would permit assessment of every modeling assumption.

The trial’s original statistical methods beyond the sponsor analyses reported in the registry record—including full covariate specifications, prespecified multiplicity control, and the handling of missing endpoint data—are not reported in the registry record. Therefore, the posted statistics support a focused reading of recorded endpoints and comparisons, not a complete audit of the analysis.

11. Confidence Intervals and Precision

The primary-outcome recalculated risk differences have 95% confidence intervals. For BIBR 1048 150 mg twice daily versus 50 mg twice daily, the interval is -0.155 to -0.046; for 225 mg twice daily, it is -0.181 to -0.076; and for 300 mg once daily, it is -0.159 to -0.050. Each of these intervals is below zero. In contrast, the enoxaparin comparison interval is -0.101 to 0.015 and includes zero. These statements refer to the unadjusted recalculations, not the sponsor’s adjusted model.

Intervals communicate the range of effect estimates compatible with the data under the calculation’s assumptions. Wider intervals indicate less precision than narrower intervals on the same scale. The enoxaparin comparison is less conclusive about the direction of the risk difference because its interval crosses zero; that does not demonstrate equivalence. The intervals for BIBR dose comparisons exclude zero, but statistical precision does not determine whether a difference is clinically important.

The sponsor’s primary logistic-regression results are odds ratios with 95% confidence intervals: 0.375 (0.244 to 0.577) for 225 mg twice daily versus 50 mg twice daily, and 0.518 (0.344 to 0.778) for 150 mg twice daily versus 50 mg twice daily. These estimates and intervals belong to the sponsor’s analysis and should not be conflated with the recalculated risk differences. Full model details are not reported in the registry record. Neither set of intervals captures uncertainty from unreported analysis choices or multiplicity across outcomes.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrative calculations based on the observed effects, not the trial’s original design assumptions. For these binary participant-with-an-event comparisons, the figures are participants per arm, not total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column indicates the calculated participants per arm for an illustrative future comparison to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm. These values are planning illustrations, not observed power.

The rows use the full observed effect and reduced fractions of that effect. Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants per arm as the target effect becomes smaller. For example, in the 225 mg twice-daily comparison with the 50 mg twice-daily reference, planning for 100% of the observed effect gives 131 participants per arm for 80% power and 174 for 90% power. Planning for 50% of the observed effect gives 602 participants per arm for 80% power and 806 for 90% power. These calculations should not be interpreted as recommendations or as evidence about the actual trial’s power; they depend on the observed effect, which may not match the effect in a future study.

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 = 0.231; treatment proportion p₁ = 0.131; average p̄ = 0.181.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5444 = 1.0670.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5398 = 0.4543.
4. n = (1.0670 + 0.4543)² / (-0.1005)² = 229.1, rounded up to 230 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 <- 0.231182795698925                          # control proportion
p1 <- 0.130666666666667                          # 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(1225822)
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 = 230 (80% power), 307 (90% power)
 75% of observed effect: n per arm = 430 (80% power), 575 (90% power)
 50% of observed effect: n per arm = 1,016 (80% power), 1,360 (90% power)
power.prop.test: 229.1 
Simulated power at n = 230 per arm: 0.808 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s posted primary analyses use logistic regression and report odds ratios for selected group comparisons. Against the BIBR 1048 50 mg twice-daily reference, the sponsor reports an odds ratio of 0.375 (95% CI 0.244 to 0.577; p < 0.001) for 225 mg twice daily and 0.518 (95% CI 0.344 to 0.778; p = 0.002) for 150 mg twice daily. The sponsor also reports comparisons with enoxaparin: 225 mg twice daily versus enoxaparin has an odds ratio of 0.469 (95% CI 0.302 to 0.727; p < 0.001), and 150 mg twice daily versus enoxaparin has an odds ratio of 0.647 (95% CI 0.427 to 0.98; p = 0.040).

The recalculations use posted summary counts to estimate unadjusted risk differences and related statistics. They are not identical to the sponsor’s regression estimates. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence for the trial’s inferential conclusion. The covariates and full model specification are not reported in the registry record, limiting a direct explanation of the difference. The recalculated results are best treated as supplementary summaries, not as corrections to or replacements for the sponsor’s model.

15. Multiplicity, Missing Data and Analysis Populations

The registry records 11 outcome measures and 36 analyses, and it lists nine posted secondary outcomes. Testing many outcomes and group comparisons increases the chance that some apparently notable findings arise by chance. A multiplicity plan can address this through approaches such as adjusting significance thresholds, controlling a family-wise error rate, or defining a hierarchy of primary and secondary tests. Those are general statistical options; the registry record does not report which approach, if any, the trial used.

The sponsor’s logistic-regression p-values and the unadjusted recalculated p-values should therefore be interpreted in light of this missing information. A small p-value for an individual analysis does not by itself establish that the result remains statistically significant after accounting for all analyses. The registry record does not report a complete prespecified analysis plan, the number of planned comparisons, or whether the posted analyses represent all planned tests.

The primary Full Analysis Set is defined as randomized patients who received at least one subcutaneous injection and one oral dose of study medication and had confirmed VTE data after surgery. This definition clarifies who contributed to the primary outcome analysis, but the record does not report how many randomized patients were excluded from that set, the reasons for missing or unconfirmed VTE data, or the methods used to handle missing outcomes. It also does not report imputation methods or sensitivity analyses for missing endpoint data. Missingness can affect comparisons if the chance of having an evaluable outcome differs between groups or is related to outcome status.

The sponsor’s full model specification, covariate adjustment, treatment of protocol deviations, and analysis of missing data are not reported in the registry record. Consequently, the available results allow description of the posted estimates but not a comprehensive assessment of robustness. These omissions matter especially when interpreting secondary outcomes and when comparing adjusted sponsor estimates with unadjusted recalculations.

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: venous thrombosis deep limb (1.3%), wound infection nec (0.8%), joint dislocation nec (0.8%), post procedural haemorrhage (0.8%), pulmonary embolism (0.8%).

The registry posts serious adverse-event counts and other adverse-event counts by treatment group. Serious adverse events affected 25 participants in the BIBR 1048 50 mg twice-daily group, 29 in the 150 mg twice-daily group, 21 in the 225 mg twice-daily group, 33 in the 300 mg once-daily group, and 31 in the enoxaparin group. The corresponding at-risk counts are 389, 390, 393, 385, and 392. These are group-level counts, not a formal comparison of treatment-related risk.

The most frequent serious-event terms listed include venous thrombosis deep limb (1.3%), wound infection NEC (0.8%), joint dislocation NEC (0.8%), post procedural haemorrhage (0.8%), pulmonary embolism (0.8%), and deep venous thrombosis NOS (0.8%). These terms are the registry’s listed serious-event summaries; they do not establish causation by study medication. Other adverse events affected 242, 267, 256, 267, and 258 participants across the same groups. Death counts are not reported in the registry record. The figures alone do not establish comparative safety, and the record’s available adverse-event summaries do not provide a complete clinical assessment.

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

The posted results describe VTE event counts over a short treatment period in patients undergoing primary elective total hip or knee replacement. In the primary Full Analysis Set, the counts were lower in the BIBR 1048 150 mg twice-daily, 225 mg twice-daily, and 300 mg once-daily groups than in the BIBR 1048 50 mg twice-daily reference group. The sponsor’s logistic-regression analyses also report lower odds for selected comparisons with that reference. Those statements summarize the recorded endpoint and analyses; they are not advice about treatment.

The comparison with enoxaparin depends on which analysis is being described. The unadjusted recalculation against the 50 mg twice-daily reference has a confidence interval that includes zero. The sponsor’s adjusted logistic-regression analyses report selected BIBR 1048 versus enoxaparin comparisons, with the details and estimates stated in the sponsor results. Because a discrepancy is flagged, the sponsor’s own analyses take precedence over recalculations from summary counts. The registry does not provide enough information to fully reconcile the estimates.

These results do not establish the best dose, a complete dose-response relationship, or comparative effects beyond the trial’s endpoint window. Nor do event counts alone establish clinical importance, long-term outcomes, or the balance of benefits and harms. The study included several regimens and outcomes, and the multiplicity strategy is not reported in the registry record. The posted safety counts also cannot on their own establish causality or comparative safety.

Interpretation should remain tied to the enrolled surgical population, the Full Analysis Set definition, the event ascertainment methods, and the treatment-period follow-up. Generalization to other populations, procedures, treatment durations, or clinical settings is not established by this record.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares several dose regimens within a randomized, double-masked, parallel-group design and records a clinically focused VTE endpoint after elective hip or knee replacement. The primary outcome combines imaging-detected DVT with symptomatic DVT and objectively confirmed pulmonary embolism. That definition illustrates how endpoint construction shapes both event counts and interpretation: a composite can capture more than symptomatic events alone, but its components may differ in clinical presentation and frequency.

The posted counts permit transparent unadjusted comparisons, while the sponsor analyses illustrate a different approach using logistic regression. Reading both makes clear why effect measures and analysis choices matter: risk differences describe absolute contrasts in event proportions, whereas odds ratios express a relative comparison of odds. The registry flags a discrepancy between the sponsor analysis and recalculations, making it important not to treat a simple recomputation as a replacement for the reported trial analysis.

The trial also highlights the distinction between statistical evidence and precision. Confidence intervals convey uncertainty, and the sample-size illustrations show how planning requirements depend on the effect one aims to detect. The original sample-size justification is not reported in the registry record, so those illustrations must not be mistaken for the study’s design rationale or observed power.

Finally, the many listed outcomes and analyses make multiplicity, missing data, and analysis-population definitions central to responsible interpretation. The registry gives useful outcome counts and selected sponsor analyses, but does not report all details needed for a full statistical audit. This is a practical example of how design, endpoint definition, model choice, and reporting completeness shape the strength of conclusions that can be drawn.

19. Limitations

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

Several trial-specific limitations affect interpretation. The primary endpoint was assessed during a short treatment period, up to the day 8 ± 2 days visit. The record does not establish longer-term VTE outcomes or recurrence. The primary measure combines venography-detected DVT with symptomatic DVT and objectively confirmed pulmonary embolism, so it aggregates events identified through different routes. Component-specific primary outcome results are not reported in the primary outcome entry.

The Full Analysis Set required receipt of both oral and subcutaneous study medication and confirmed post-surgery VTE data. It therefore does not simply include every randomized participant. The number and characteristics of patients not meeting this definition, reasons for missing or unconfirmed outcome data, and missing-data sensitivity analyses are not reported in the registry record.

The registry includes multiple doses, outcomes, and analyses, but the multiplicity strategy and complete prespecified analysis plan are not reported. The sponsor’s logistic-regression model details are also not reported, limiting evaluation of adjustment choices and direct reconciliation with unadjusted calculations. The record explicitly flags a discrepancy, so sponsor analyses take precedence for inferential interpretation.

There is a wording inconsistency for the once-daily BIBR 1048 regimen: the arm label says 300 mg once daily, while its detailed intervention description specifies BIBR 1048 150 mg once daily. The registry also does not report a sample-size justification, full allocation procedures, or a complete account of adverse-event attribution. These gaps constrain conclusions about dose-response, safety, and generalizability beyond the recorded population and follow-up.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BIBR 1048 Dose Range Finding Study in Prevention of Venous Thromboembolism in Patients With Primary Elective Total Hip or Knee Replacement Surgery — NCT01225822.
• Registry record last updated 2014-05-19; status last verified 2014-02.
• Results first posted 2010-12-16.
• 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 randomized, double-masked, parallel-group Phase 2 study of BIBR 1048 regimens and enoxaparin in patients undergoing primary elective total hip or knee replacement. Enrollment was 1973. The primary endpoint was the number of participants with VTE events during the treatment period, assessed in a defined Full Analysis Set.

Posted primary counts and sponsor logistic-regression analyses are available, alongside selected secondary outcomes and adverse-event summaries. Simple unadjusted recalculations are also available, but the record flags a discrepancy; the sponsor’s own analysis takes precedence for inferential results. The original sample-size justification, multiplicity strategy, full model details, and missing-data methods are not reported in the registry record. Interpretation is therefore limited to the stated endpoints, analysis populations, and follow-up.