A Study of DU-176b, Prevention of Venous Thromboembolism in Patients After Total Hip Arthroplasty: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of DU-176b, Prevention of Venous Thromboembolism in Patients After Total Hip Arthroplasty (NCT01181167), a randomized phase 3 study. The primary outcome is Incidence of Subjects With Venous Thromboembolism Events.

2. Clinical Question

3. Trial Design

NCT01181167, titled “A Study of DU-176b, Prevention of Venous Thromboembolism in Patients After Total Hip Arthroplasty,” is listed as a phase 3 randomized trial with a parallel design. The official title identifies it as the STARS J-5 Trial and describes a double-blind, double-dummy comparison of oral DU-176b with enoxaparin sodium. Masking is listed as quadruple. The registry record lists Daiichi Sankyo Co., Ltd. as sponsor and the trial status as completed.

The registry record gives an enrollment of 610. It lists a start date of 2009-05 and primary completion of 2010-01. These dates describe the registry’s recorded timing; they do not establish when all analyses were completed or results were posted. The original protocol details beyond the registry fields are not reported in the registry record.

The DU-176b regimen was an oral 30 mg dose once daily for 2 weeks, started within 6 to 24 hours after surgery. The enoxaparin sodium regimen was a subcutaneous 20mg(=2000IU)/0.2ml injection twice daily for 2 weeks, started within 24 to 36 hours after surgery. The double-dummy description indicates that the trial design used dummy treatments to support masking when comparing oral and injectable regimens; further operational details are not reported in the registry record.

The efficacy results are reported for the FAS, while the posted bleeding and safety results use larger arm denominators. The registry definition of the FAS includes exclusions related to GCP violations, receipt of study drug, symptoms, and appropriate venography. The specific disposition of all enrolled participants and reasons for any differences between analysis populations are not reported in the registry record. These distinctions matter when interpreting endpoint percentages because each result applies to its stated population rather than automatically to every enrolled participant.

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: The FAS was defined as all subjects enrolled in the study, but excluded those who had significant GCP violations, who had not received any doses of the study drug, or those who did not develop symptomatic DVT or PE, but in whom venography was not appropriately performed.

5. Baseline Characteristics

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

Population: Number of baseline participants reflects the efficacy analysis population.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Subjects With Venous Thromboembolism Events, measured over 2 weeks.

The primary endpoint was the incidence of subjects with venous thromboembolism events over 2 weeks. It was defined as the proportion of participants who experienced at least one qualifying event between starting study treatment and venography at the end of treatment. Qualifying events included lower extremity DVT confirmed by bilateral venography at the end of treatment, definite symptomatic PE, or symptomatic DVT confirmed before the end-of-treatment venography.

This composite endpoint combines events identified through scheduled venography with clinically symptomatic events. In general, a composite can capture more than one relevant manifestation of the condition under study, but its interpretation depends on the definitions and ascertainment of each component. The registry record does not provide separate results for each component, so the posted primary result cannot show which component contributed most to the overall incidence.

The endpoint is expressed as a percentage of participants with at least one event, rather than as an event rate over person-time. Each participant contributes to the endpoint according to whether at least one qualifying event occurred during the defined period. The registry specifies a 95% confidence interval for the arm percentages. The primary efficacy population was the FAS, with exclusions described in the registry definition. Because the endpoint relies in part on venography, the completeness and appropriateness of that assessment are relevant to inclusion in the efficacy population.

7. Results Posted in the Registry

• Enoxaparin Sodium: 6.9% (17/248) versus 2.4% (6/255) on control; risk difference 4.5 percentage points (95% CI 0.8 to 8.2), risk ratio 2.91 (1.17–7.27); unadjusted two-proportion z-test p = 0.016.

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.

Incidence of Major Bleeding or Clinically Relevant Non-major Bleeding

• 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:
  • Enoxaparin Sodium: 3.7% (11/301) versus 2.6% (8/303) on control; risk difference 1.0 percentage points (95% CI -1.8 to 3.8), risk ratio 1.38 (0.56–3.39); unadjusted two-proportion z-test p = 0.475.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enoxaparin Sodium and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: the incidence of major bleeding or clinically relevant non-major bleeding during 2 weeks. Its purpose differs from that of the primary endpoint, which concerns venous thromboembolism. Reading both outcomes together gives a broader view of the outcomes the registry reports, but the secondary result does not determine the primary non-inferiority conclusion.

The secondary comparison is less conclusive statistically than a simple claim of equal bleeding outcomes would suggest. Its unadjusted confidence interval includes zero, and its unadjusted p-value is 0.475. This pattern means the posted estimate is uncertain and compatible with more than one direction of difference. It is not evidence that the groups are equivalent on the bleeding endpoint.

There is only one secondary endpoint posted, so the registry results do not establish a broader pattern across multiple secondary outcomes. The primary and secondary endpoints also use different analysis populations, as reflected in their arm denominators. That difference should be kept in mind when comparing their estimates; the endpoints are not interchangeable measures of a single outcome.

In general, secondary analyses often carry less evidential weight than the primary analysis when they are not the main basis for the trial’s question. Multiple outcome testing can increase the chance of finding apparently notable results by chance if multiplicity is not addressed. The registry record does not report a multiplicity adjustment or a hierarchy for secondary testing. The secondary finding should therefore be treated as supportive descriptive information, not as a standalone basis for an efficacy or safety conclusion. Details of the endpoint-specific point estimates remain available in the posted results and should be interpreted with their confidence intervals rather than as definitive proof of either difference or equivalence.

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

• Incidence of Major Bleeding or Clinically Relevant Non-major Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

The posted statistics combine arm-level event percentages, confidence intervals, a recalculated unadjusted comparison, and the sponsor’s reported non-inferiority analysis. Each answers a somewhat different statistical question. The arm percentages describe the observed frequency of participants with an event in each group. A risk difference compares those frequencies on an absolute scale. The sponsor analysis is identified separately and should be interpreted according to its own method and non-inferiority framework.

What does an event percentage describe?

For a binary endpoint, each participant is classified according to whether the defined event occurred during the stated period. The percentage is the proportion of participants in the analysis population who experienced at least one event. This is a participant-level summary: multiple events in the same person do not make that person count as multiple participants with the endpoint. In these results, the primary endpoint is based on the FAS and covers the 2-week treatment period.

The meaning of the percentage depends on who is included in its denominator and how events are identified. The registry’s FAS definition includes exclusions involving GCP violations, not receiving study drug, and missing appropriate venography in participants without symptomatic DVT or PE. The registry also reports bleeding results for different arm denominators. Estimates from populations with different inclusion rules or denominators should not be treated as directly interchangeable.

What does a risk difference express?

A risk difference expresses the absolute separation between two event proportions. The recalculated comparison labels enoxaparin sodium as the comparison arm and DU-176b as the control arm; its positive estimate therefore represents the enoxaparin sodium proportion minus the DU-176b proportion. The estimate is unadjusted, meaning it is calculated from the posted arm-level summary data rather than from a covariate-adjusted model. It is useful for describing the absolute contrast in the observed data, but it is not the same estimand as every model-based analysis.

Relative measures such as a risk ratio or odds ratio express the comparison on a relative scale rather than as an absolute difference. These measures can help describe the same binary outcome from another perspective, but their values depend on the scale and method used. The registry’s recalculated measures do not override the sponsor’s prespecified analysis.

Why are confidence intervals useful?

In general, a confidence interval describes the range of estimates compatible with the data and the method’s assumptions at the stated confidence level. It communicates uncertainty more directly than a single point estimate. A wider interval indicates less precision; an interval may include values corresponding to no difference as well as values suggesting a difference. A confidence interval is not a guarantee that the true value lies inside its particular bounds, and it does not alone determine whether a non-inferiority criterion has been met.

The arm-level 95% confidence intervals describe uncertainty around each event percentage. The recalculated 95% confidence interval for the risk difference describes uncertainty around that absolute comparison. A comparison interval is generally the more direct interval for assessing the contrast between groups; overlapping arm-specific intervals are not, by themselves, a formal test of the between-group difference.

How should the sponsor analysis be distinguished?

The registry identifies the sponsor’s analysis as ANCOVA, with a Cox Proportional Hazard parameter, and marks the result as a non-inferiority or equivalence analysis. These labels are reported as recorded; the registry does not provide the model specification, covariates, non-inferiority margin, or confidence interval for this analysis. A p-value alone does not supply those missing details. For non-inferiority, the interpretation depends on a prespecified margin and the direction and uncertainty of the treatment contrast, so the posted p-value should not be used to infer an unreported margin.

The sponsor result and the simple recalculation are not necessarily expected to match: they may use different populations, methods, scales, or analysis assumptions. The registry record flags a discrepancy. In that circumstance, the sponsor’s own analysis takes precedence over the simple unadjusted recalculation for understanding the trial’s reported primary conclusion. The recalculation remains descriptive and helps readers see the contrast implied by the posted summary counts.

Why can binary outcomes be statistically challenging?

In general, binary outcomes with few events can yield imprecise estimates, because a small change in the event count can materially affect the percentage or comparison. The interval reflects this sampling uncertainty, subject to the method used. Statistical significance and clinical importance are distinct concepts: a p-value describes compatibility with a specified null model under its assumptions, not the size or importance of an effect. The registry does not provide an independent clinical threshold for interpreting the magnitude of the observed contrasts.

In general, over-dispersion arises when outcome variability exceeds what a chosen model assumes. If a model fails to account for that extra variability, standard errors and uncertainty estimates may be too small. The registry record does not report whether over-dispersion was assessed or relevant to the sponsor’s model, so no conclusion about it can be drawn for this trial.

11. Confidence Intervals and Precision

The primary arm percentages are 2.4% for DU-176b and 6.9% for enoxaparin sodium. Their reported 95% confidence intervals are 1.1% to 5.0% and 4.3% to 10.7%, respectively. These intervals convey uncertainty in each arm’s event percentage; they are not a confidence interval for the difference between arms.

For the recalculated risk difference, the estimate is 0.045 and the 95% confidence interval is 0.009 to 0.082. The interval lies above zero on the stated comparison scale. The recalculated estimate and interval are unadjusted and should be interpreted separately from the sponsor’s non-inferiority analysis, for which the registry does not report confidence bounds. The sponsor’s analysis reports a p-value of <0.001, but a p-value does not communicate the range of plausible treatment contrasts or substitute for the missing interval and non-inferiority margin.

The confidence interval for the secondary bleeding risk difference extends from -0.018 to 0.038. Because it includes zero, the posted summary data are compatible with no absolute difference as well as with differences in either direction under that recalculation. The interval also permits a range of effect sizes, so the point estimate alone would overstate the precision of the comparison.

In general, confidence intervals are most informative when read alongside the point estimate, the outcome definition, the population, and the analysis method. They quantify statistical uncertainty under the chosen method, not uncertainty from unreported design choices, missing data, measurement quality, or generalizability. The registry record does not report all details needed to assess those other sources of uncertainty.

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 a record of the trial’s original sample-size design. For these binary outcomes, the figures are participants per arm, not total events. The stated assumptions 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 to the stated fraction of the observed effect.

The 80% power column gives the calculated participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if the assumptions and effect were correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. They are planning illustrations, not observed power. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

Each planning row uses a different fraction of the observed effect. Planning for 100% of the observed primary effect gives 339 participants per arm for 80% power and 454 participants per arm for 90% power. Planning for 75% of the observed effect gives 533 participants per arm for 80% power and 713 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,040 participants per arm for 80% power and 1,391 participants per arm for 90% power. The smaller-effect rows require more participants because smaller differences are harder to distinguish from random variation.

The same principle applies to the secondary bleeding outcome, where the planning figures are much larger because the observed effect used in the illustration is smaller. These calculations should not be read as evidence that the completed trial was adequately or inadequately designed: that assessment requires the original assumptions, which are not reported in the registry record. The displayed calculations also do not account for departures from their stated planning assumptions.

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 = 0.024; treatment proportion p₁ = 0.069; average p̄ = 0.046.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2964 = 0.5809.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2947 = 0.2480.
4. n = (0.5809 + 0.2480)² / (0.0450)² = 339.0, rounded up to 339 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 <- 0.0235294117647059                          # control proportion
p1 <- 0.0685483870967742                          # 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(1181167)
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 = 339 (80% power), 454 (90% power)
 75% of observed effect: n per arm = 533 (80% power), 713 (90% power)
 50% of observed effect: n per arm = 1,040 (80% power), 1,391 (90% power)
power.prop.test: 339 
Simulated power at n = 339 per arm: 0.822 (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 primary analysis is reported as a non-inferiority or equivalence analysis, with ANCOVA listed as the method and Cox Proportional Hazard as the parameter. The reported value is -4.5, and the reported p-value is <0.001. The registry record does not give a confidence interval for this analysis or state the non-inferiority margin and decision rule. Consequently, the sponsor result can be described as the registry’s reported non-inferiority analysis, but its full interpretation cannot be reconstructed from the posted fields alone.

The unadjusted recalculation uses the posted arm-level event summaries to estimate an absolute risk difference and its uncertainty. It is not a reproduction of the sponsor’s model-based analysis. The registry record flags a discrepancy between the posted results and the recalculation. In that situation, the sponsor’s own analysis takes precedence for interpreting the trial’s stated primary analysis. The recalculation can still provide a transparent descriptive comparison, but it should not be substituted for the sponsor’s analysis or used to reverse its conclusion.

The registry record does not report enough detail to identify the source of the discrepancy. It would be inappropriate to speculate about whether it reflects different analysis populations, model choices, outcome handling, or another cause.

15. Multiplicity, Missing Data and Analysis Populations

The registry record reports one primary endpoint and one posted secondary endpoint. It identifies the sponsor’s primary analysis as non-inferiority or equivalence, but does not report the non-inferiority margin, the full hypothesis-testing procedure, or a detailed statistical analysis plan. It also does not state whether the secondary endpoint was included in a formal testing hierarchy or whether any multiplicity adjustment was applied.

In general, multiplicity concerns arise when several hypotheses or outcomes are tested. Without an appropriate strategy, the chance of at least one apparently notable result can rise as the number of tests increases. A planned hierarchy or adjustment can define how evidence is evaluated across outcomes. Because the registry record does not report such details, the secondary p-value should be read as unadjusted and exploratory in evidential weight, not as a result known to control an overall error rate.

The registry provides an FAS definition for the primary efficacy endpoint, including exclusions related to GCP violations, study-drug exposure, and venography. It does not provide a full participant flow, counts and reasons for missing endpoint data, or sensitivity analyses for the handling of missing observations. It is therefore not possible to assess from the registry record alone how alternative missing-data assumptions might affect the primary result. The endpoint’s reliance in part on venography makes ascertainment and inclusion relevant, but the record does not provide further detail about missing assessments.

The record also does not report whether the analysis was intention-to-treat, per-protocol, or another formally defined analysis set beyond its stated FAS description. Nor does it report whether the sponsor used additional populations for the non-inferiority assessment. Those details can matter in non-inferiority trials, because the result may depend on adherence, exclusions, and the analysis population. These are reporting gaps; they do not establish that any particular analysis was or was not performed.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: femur fracture (0.7%), dislocation of joint prosthesis (0.7%), deep vein thrombosis (0.3%), intestinal obstruction (0.3%), postoperative wound infection (0.3%).

The serious adverse event figures list 9 affected participants in each group. The denominators are 303 for DU-176b and 301 for enoxaparin sodium. The registry also lists other adverse events affecting 197 participants in the DU-176b group and 232 participants in the enoxaparin sodium group. These are separate registry summaries, and the record does not provide further definitions or analysis details in the posted safety fields.

The serious adverse event terms listed most often include femur fracture and dislocation of joint prosthesis, each at 0.7%; deep vein thrombosis, intestinal obstruction, postoperative wound infection, and hip fracture are each listed at 0.3%. These terms are registry-listed summaries, not a complete account of all safety outcomes or an adjusted comparison between groups. The figures should be read with the stated denominators and the limited reporting detail in mind.

Deaths are not reported in the registry record. The adverse-event data do not establish that an event was caused by study treatment, and the posted summaries alone do not support a comprehensive comparative safety assessment.

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

The primary endpoint results describe a lower observed proportion of participants with qualifying venous thromboembolism events in the DU-176b arm than in the enoxaparin sodium arm in the stated FAS. The recalculated absolute comparison and the sponsor’s reported non-inferiority analysis are distinct analyses. The sponsor analysis is the relevant registry result for the trial’s stated non-inferiority question, while the recalculation is an unadjusted description of the posted arm summaries.

The registry record marks the sponsor analysis as non-inferiority or equivalence and reports p <0.001. However, it does not state the non-inferiority margin or provide a confidence interval for the sponsor analysis. Without those details, the full criterion used to support a non-inferiority interpretation cannot be independently assessed from the registry record. The reported analysis should not be expanded into a claim about an unreported margin or protocol decision rule.

The primary results apply to the endpoint definition, treatment schedules, follow-up period, and FAS described in the record. They do not directly answer questions about other regimens, other patient groups, longer follow-up, individual endpoint components, or outcomes not posted in the registry. The registry reports a composite endpoint, and it does not give separate results for the individual event types that make up that composite.

The secondary bleeding result is uncertain and does not establish equivalence between groups. The safety summaries likewise do not show causation or provide a complete account of comparative risk. Statistical findings should be distinguished from clinical decisions: these results describe the posted trial data and their precision, and do not constitute medical advice.

In general, a trial result is most informative when its endpoint, population, analysis plan, and uncertainty are considered together. Here, some of those elements are reported, while the original sample-size justification, full statistical plan, non-inferiority margin, and detailed missing-data handling are not reported in the registry record. Those omissions limit how completely the sponsor’s conclusion can be independently evaluated.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis scale and the trial question matter. The primary outcome is binary: a participant either experienced at least one qualifying venous thromboembolism event during the defined period or did not. The arm percentages provide an accessible summary, while the recalculated risk difference describes the absolute contrast. Neither is automatically interchangeable with the sponsor’s non-inferiority model.

Non-inferiority is not established merely by observing a favorable event percentage or a small p-value. In general, it requires comparison against a prespecified margin under a defined analysis plan. The registry record identifies a non-inferiority analysis but does not report the margin or its confidence interval. This makes the distinction between the sponsor’s recorded conclusion and what can be independently reconstructed from the registry especially important.

The registry also demonstrates why precision matters. The event counts are limited, and the confidence intervals show uncertainty around the percentages and recalculated contrast. Looking at the interval alongside the point estimate avoids treating a single summary as an exact effect. The secondary endpoint reinforces that an uncertain comparison should not be mistaken for proof of no difference.

Finally, the primary efficacy population and the safety/bleeding populations have different denominators. Clear separation of populations, endpoint definitions, and analysis methods helps prevent misinterpretation. The registry’s omissions around multiplicity, missing data, and original sample-size planning further show why statistical reporting is part of evaluating evidence, not merely a technical supplement to the reported result.

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.

The registry does not report the non-inferiority margin or provide a confidence interval for the sponsor’s primary analysis. The reported method and parameter labels do not include enough detail to reproduce the analysis or assess its full decision rule. The discrepancy flag also means the unadjusted recalculation should not be treated as replacing the sponsor result; the reason for the discrepancy is not reported in the registry record.

The FAS definition is available, but a full participant flow, exclusions by arm, and detailed missing-data handling are not reported. The primary endpoint includes events established through venography and symptomatic events, yet component-specific results are not posted. The record therefore does not show how the overall endpoint was distributed across its different event components.

The original sample-size rationale, the trial’s planned statistical assumptions, and any interim analyses are not reported in the registry record. The planning calculations based on the observed effect cannot substitute for that design information. Similarly, the registry does not report a complete multiplicity strategy or a detailed hierarchy for secondary outcomes.

Safety reporting is limited to the posted summaries. The registry does not report deaths, detailed event narratives, or information sufficient to determine causality. The trial’s recorded 2-week treatment and endpoint periods also constrain interpretation to that timeframe; longer-term outcomes are not reported in the registry record. These limitations identify what the posted information cannot resolve and do not establish that the missing procedures or analyses were not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of DU-176b, Prevention of Venous Thromboembolism in Patients After Total Hip Arthroplasty — NCT01181167.
• Registry record last updated 2019-03-05; status last verified 2015-02.
• Results first posted 2015-01-26.
• 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

NCT01181167 is a completed phase 3 randomized, parallel-group trial comparing DU-176b with enoxaparin sodium after elective total hip arthroplasty. The registry lists quadruple masking and a double-dummy design, with 610 participants enrolled. The primary endpoint was the incidence of participants with at least one qualifying venous thromboembolism event during 2 weeks.

The registry reports arm-level primary results and a sponsor non-inferiority analysis, alongside one secondary bleeding endpoint and safety summaries. The sponsor analysis takes precedence over the flagged unadjusted recalculation for interpreting the trial’s reported primary analysis. The registry does not report the non-inferiority margin, full statistical plan, original sample-size justification, or detailed missing-data handling, limiting independent assessment of some aspects of the result.