BAX 855 PK-guided Dosing: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BAX 855 PK-guided Dosing (NCT02585960), a randomized phase 3 study. The primary outcome is Percentage of Participants With a Total Annualized Bleeding Rate (ABR) of Zero for Second Six Months.

2. Clinical Question

3. Trial Design

The registry identifies this as a phase 3, prospective, randomized, multicenter, parallel-group study. It was open label, with no masking reported. Enrollment was 135. The registry lists the study as completed, with a start date of 2015-11-23 and primary completion on 2018-08-05.

Participants first underwent an initial pharmacokinetic assessment. They were then randomized to one of two BAX 855 prophylaxis regimens: a target FVIII trough level of 1-3%, or a target of 8-12%. The trial description calls these the standard and intensified treatment arms, respectively. Because both groups received BAX 855, the randomized comparison concerns the dosing targets rather than BAX 855 versus a different treatment.

The primary outcome was evaluated in the full analysis set. The registry defines that set as participants randomized to one of the prophylactic arms who received prophylactic treatment for any period of time. The primary endpoint covers Day 183 to Day 364, described as six months. For this endpoint, the registry reports 57 participants in the low-level arm and 58 in the high-level arm.

The record also lists a non-randomized BAX 855 group for pharmacokinetic evaluation. Its safety record includes 6 participants. It should not be treated as a third randomized comparison group for the primary endpoint. The registry does not report detailed eligibility criteria, the allocation sequence method, or the original design assumptions for sample size.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 135 participants were enrolled in the study. Of them,14 participants were dropped out and did not receive any treatment 121 participants underwent initial pharmacokinetic(PK) assessment with a single administration of BAX 855 and based on their individual PK values, 115 participants were randomized to any one of the prophylactic regimen.

PK/Safety Assessment Period

Reasons for not completing this period:

Prophylactic Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all participants who were randomized to one of the two prophylactic arms and treated prophylactically for any period of time.

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: Safety Analysis Set (SAS) included all participants enrolled who had at least one BAX 855 infusion.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With a Total Annualized Bleeding Rate (ABR) of Zero for Second Six Months, measured over Day 183 to Day 364 (6 months).

The primary endpoint is the percentage of participants with a total annualized bleeding rate of zero during Day 183 to Day 364. An annualized bleeding rate expresses bleeding over an observation period in years; the registry says it was determined by dividing the number of bleeds by the observation period in years. For this endpoint, a value of zero identifies participants with no recorded bleeds in the specified period.

A proportion with no events provides one way to describe bleeding outcomes: it shows how many participants reached a period without a recorded bleed, rather than summarizing the number of bleeds across all participants. That distinction matters because the percentage with zero bleeds and the mean annualized bleeding rate capture different features of the outcome distribution. The registry also lists mean bleeding rates as secondary outcomes.

The time window is restricted to the second six months, rather than the entire study period. The endpoint therefore addresses the proportion with no bleeds in that defined interval. It does not by itself describe bleeding before Day 183, changes over time, or the overall distribution of bleed counts. The registry record does not report further details about how observation time or missing endpoint data were handled.

7. Results Posted in the Registry

• BAX 855-High Level: 62.1% (36/58) versus 42.1% (24/57) on control; risk difference 20.0 percentage points (95% CI 2.1 to 37.9), risk ratio 1.47 (1.02–2.12); unadjusted two-proportion z-test p = 0.032.

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.

Total Annualized Bleeding Rate for Second Six Months

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • BAX 855-High Level: mean 1.65 versus 3.60 on control; difference -1.95 (95% CI -4.11 to 0.20), standardized effect d = -0.33; z-test p = 0.076.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BAX 855-High Level and the control. The interval gives the range of effects that remain compatible with the data.

Annualized Spontaneous Bleeding Rate for Second Six Months

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • BAX 855 - High Level: mean 0.74 versus 2.49 on control; difference -1.75 (95% CI -3.52 to 0.01), standardized effect d = -0.36; z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BAX 855 - High Level and the control. The interval gives the range of effects that remain compatible with the data.

Annualized Traumatic Bleeding Rate for Second Six Months

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • BAX 855-High Level: mean 0.91 versus 1.11 on control; difference -0.20 (95% CI -1.09 to 0.69), standardized effect d = -0.09; z-test p = 0.655.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BAX 855-High Level and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 25 secondary endpoints, including total, spontaneous, traumatic, and joint bleeding outcomes, as well as consumption and treatment of bleeding episodes. Numerical summaries are available for three annualized bleeding-rate outcomes for the second six months. In each of those three comparisons, the mean rate is lower in the high-level group than in the low-level group. The size and precision of those differences vary, and their unadjusted intervals include zero.

This broad directional pattern is consistent with the primary descriptive result, where a higher percentage of the high-level group had zero annualized bleeding in the specified period. The endpoints are not interchangeable, however. The primary endpoint asks whether a participant had a rate of zero; the secondary mean rates summarize the average number of bleeds annualized over observation time. A group can differ on one summary without showing the same degree of separation on another.

These secondary comparisons carry less inferential weight than a prespecified primary analysis. The registry lists many outcomes, and testing multiple endpoints creates more opportunities for apparently notable results by chance. The record does not report a multiplicity adjustment or a hierarchy for interpreting secondary results. The listed secondary p-values are unadjusted recalculations, not sponsor-reported analyses in the record, so they should be treated as exploratory evidence rather than as independent confirmation of the primary result.

Numerical results for the other listed secondary endpoints are not reported in the registry record. Without those data, it is not possible to characterize the full secondary outcome pattern or determine whether it is consistent across all endpoint types. The available secondary summaries offer context, but they do not resolve the discrepancy between the sponsor’s primary analysis and the simple recalculation.

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

• Total Annualized Bleeding Rate for Second Six Months
• Annualized Spontaneous Bleeding Rate for Second Six Months
• Annualized Traumatic Bleeding Rate for Second Six Months
• Annualized Joint Bleeding Rate (AJBR) for Second Six Months
• Total Weight-adjusted Consumption of BAX 855
• Number of Bleeding Episodes: Overall Hemostatic Efficacy Rating at Number of Infusions
• Number of Bleeding Episodes: Overall Hemostatic Efficacy Rating at Bleed Resolution
• Treatment of Bleeding Episodes: Number of BAX 855 Infusions Per Bleeding Episode Required Until Bleed Resolution

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level measure: each participant either had a total annualized bleeding rate of zero in the specified period or did not. A percentage summarizes the share of participants in each group meeting that criterion. A contrast between percentages is a comparison of proportions; it is not the same quantity as a difference between average bleed rates.

What does a confidence interval communicate?

A confidence interval describes the uncertainty around an estimated contrast under the assumptions of the method used to construct it. An interval that includes zero is compatible with no difference in the direction measured, as well as with values on either side of zero. An interval that stays on one side of zero indicates that the values covered by that interval have the same direction. Neither interval width nor whether it crosses zero describes clinical importance by itself.

The registry’s primary analysis is labeled “Chi-squared” and reports a “Gaussian Statistic estimate,” with a 95% confidence interval. Those labels describe the analysis as it appears in the registry; the record does not provide enough detail to reconstruct the sponsor’s exact estimand, coding, or calculation. The posted analysis is a superiority analysis. Its reported interval spans zero, while the simple recalculation’s interval excludes zero. Because the discrepancy is flagged, the sponsor’s own analysis takes precedence over the recalculation.

Why distinguish the posted analysis from a recalculation?

A simple unadjusted recalculation uses posted summary counts to form a direct comparison of the groups. It does not necessarily reproduce the trial’s planned model, analysis population implementation, or other choices. The registry’s analysis may reflect an approach not recoverable from the summary data alone. The record does not report enough information to explain the difference, so the recalculation should be read as a check on the posted summaries, not as an alternative official result.

Why can bleeding-rate data be difficult to summarize?

The secondary bleeding-rate outcomes are reported as means with standard deviations. A mean describes the average rate, while a standard deviation describes the spread of individual rates around that average. Bleeding counts can be unevenly distributed: many participants may have few or no events while a smaller number have more. In such settings, a mean and standard deviation do not show the full shape of the data. Over-dispersion is a general statistical concept in which observed variation is greater than a simple model would expect; it can matter for event-count analyses because standard errors and inference may depend on how variation is modeled. The registry does not report whether a count model or an over-dispersion adjustment was used for these secondary outcomes.

The secondary mean differences and p-values in the recalculation are unadjusted. They are direct comparisons based on posted summaries and should not be confused with adjusted analyses from a prespecified model. The registry does not provide sponsor-reported analyses for those secondary endpoints in the listed results. Differences in group means are descriptive unless accompanied by a suitable inferential procedure and an account of the analysis plan.

What does power mean in planning?

Power is a planning concept: under specified assumptions, it is the probability that a planned analysis would detect a particular effect if that effect were present. The sample-size illustrations use the observed effect, or a stated fraction of it, as a planning target. They assume a two-sided significance level of 0.05, equal allocation, and a normal approximation. These are assumptions for the illustrations, not information about the trial’s original design. The registry does not report the original sample-size justification or its assumptions.

The illustrations are not observed power. Once results have been observed, a power calculation based on the observed effect does not add an independent measure of certainty; the estimate and its confidence interval are more informative about the observed data. The posted planning figures are best used to understand how the implied planning requirement changes when a different effect size is targeted, not to judge whether the completed trial was adequately designed.

11. Confidence Intervals and Precision

The primary group percentages are 42.1% and 62.1%. The posted analysis reports a 95% confidence interval from -0.038 to 3.958 for its stated estimate. Because the interval includes zero, the sponsor’s analysis leaves uncertainty about whether the contrast differs from zero under the reported method. The interval’s span also indicates that a range of effects is compatible with that analysis; the endpoints should not be interpreted as a list of equally likely values.

The simple unadjusted recalculation has an interval that excludes zero, unlike the sponsor-reported interval. That difference in interval behavior is part of the flagged discrepancy and is a reason not to select the more favorable result as if it were the definitive analysis. The sponsor’s own analysis takes precedence, while the recalculation helps identify that the posted summaries and reported test do not yield the same inference.

Confidence intervals are most useful when read alongside the point estimate, the outcome definition, and the analysis method. A wide interval indicates less precision than a narrow interval on the same scale, but a confidence interval does not account for every possible source of uncertainty. It does not correct for missing data, choice of analysis, multiplicity, or limits to generalizability. The registry record does not provide enough information to assess those issues fully.

The secondary mean-rate comparisons also illustrate uncertainty: the unadjusted intervals for the three listed rate outcomes include zero. Their means and standard deviations show variation in observed rates, but the posted summaries cannot establish the shape of the underlying distributions. The record does not report confidence intervals for the individual group means, and no further precision estimates should be inferred from the summaries alone.

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 illustrations express the estimated number of participants per arm for the listed binary and continuous outcomes. They are not total event counts. The registry’s stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified target effect under those assumptions. The 90% power column gives the corresponding estimate for a 90% chance. These are planning probabilities, not probabilities that the trial’s finding is true. For each endpoint, planning for a smaller fraction of the observed effect requires more participants per arm than planning for the full observed effect. This reflects the general statistical principle that smaller effects are harder to distinguish from random variation.

The numbers are illustrations based on observed results, rather than a reconstruction of the trial’s design process. They do not establish that the study was planned using these assumptions, and they should not be read as observed power. The record does not report whether the original design included other assumptions, such as an expected control rate, allowance for losses, or an adjustment for multiple outcomes. No such assumptions can be inferred from the illustration.

When reading the accompanying curve, the relevant question is how the planning requirement changes as the targeted effect changes. A curve does not replace the stated assumptions or the uncertainty in the observed estimate. Because planning is sensitive to the effect selected, the full observed effect should not automatically be treated as a reliable future target. The alternative fractions in the illustrations make that dependence visible without determining which effect would be appropriate for 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 = 0.421; treatment proportion p₁ = 0.621; average p̄ = 0.521.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7065 = 1.3847.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6922 = 0.5826.
4. n = (1.3847 + 0.5826)² / (0.1996)² = 97.1, rounded up to 98 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 <- 0.421052631578947                          # control proportion
p1 <- 0.620689655172414                          # 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(2585960)
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 = 98 (80% power), 130 (90% power)
 75% of observed effect: n per arm = 174 (80% power), 233 (90% power)
 50% of observed effect: n per arm = 392 (80% power), 524 (90% power)
power.prop.test: 97.1 
Simulated power at n = 98 per arm: 0.816 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is a superiority analysis reported as chi-squared, with a Gaussian statistic estimate of 1.960 and a 95% confidence interval from -0.038 to 3.958. The interval spans zero. The registry also reports a p-value of 0.054. Taken together, the posted sponsor analysis does not provide clear evidence of superiority under a conventional interpretation of the reported test.

A simple unadjusted recalculation from the posted counts gives a positive risk difference and an unadjusted p-value of 0.032. Its confidence interval excludes zero, so it leads to a different conclusion about statistical evidence than the registry’s analysis. The record marks a discrepancy, but does not explain its source. Possible explanations should not be guessed.

The sponsor’s own analysis takes precedence over the simple recalculation. The recalculation is useful as a transparent check of the posted counts, but it does not replace the analysis used by the trial sponsor. The registry record does not describe enough of the statistical plan, estimator, or implementation details to determine why the results differ. Readers should therefore distinguish the observed percentages, the sponsor-reported inferential result, and the unadjusted recalculation rather than merging them into one conclusion.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists 25 secondary endpoints. It records one primary analysis. Evaluating multiple outcomes can increase the chance that at least one result appears statistically noteworthy even when there is no underlying effect. Statistical procedures can address this issue through a prespecified hierarchy or adjustment, but the registry record does not report whether such a procedure was planned or used.

The three secondary bleeding-rate comparisons are unadjusted recalculations. Their p-values should not be interpreted as if they had been adjusted for the number of outcomes examined. The record does not state a family of hypotheses, a testing order, or a multiplicity strategy. It also does not report sponsor analyses for these secondary endpoints. Consequently, the secondary findings are less secure as confirmatory evidence than a result from a documented, prespecified testing plan would be.

The primary population is defined as the full analysis set: randomized participants in either prophylactic arm who were treated prophylactically for any period of time. This definition clarifies who was included in the stated analysis population. It does not explain how participants with incomplete follow-up, missing bleed records, or other unavailable outcome data were handled. Missing-data methods are not reported in the registry record.

The record also does not report whether an interim analysis was conducted, whether any data were excluded from the primary analysis, or whether sensitivity analyses tested alternative assumptions about missing observations. These are distinct questions from the definition of the full analysis set. Without those details, the potential influence of missing data and analysis choices cannot be assessed from the registry information alone. The original statistical plan and sample-size justification are likewise not reported in the registry record.

16. Safety Results

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

Deaths

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: synovitis (1.8%), abscess limb (1.8%), appendicitis (1.8%), cellulitis (1.8%), head injury (1.8%).

For serious adverse events, the registry lists 5 affected participants among 57 at risk in the BAX 855-Low Level group and 5 among 58 at risk in the BAX 855-High Level group. The non-randomized group lists 0 affected participants among 6 at risk. The registry reports no deaths in any of these groups.

For other adverse events, the record lists 25 affected participants among 57 at risk in the low-level group and 25 among 58 at risk in the high-level group. The non-randomized group lists 0 among 6. These counts describe the participants recorded as affected; they do not establish that an event was caused by treatment. The registry does not provide event-level detail for these other events in the registry record.

The leading serious-event terms are each reported as 1.8%: synovitis, abscess limb, appendicitis, cellulitis, head injury, and radius fracture. These are registry listings, not evidence of a causal relationship to BAX 855. Safety comparisons should also be interpreted in light of the group sizes and the fact that the non-randomized participants are not part of the randomized efficacy comparison. The registry record does not report additional context such as event timing, severity beyond the serious classification, or attribution assessments.

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

The posted primary percentages show that a greater share of participants in the high-level arm than in the low-level arm had a total annualized bleeding rate of zero during the second six months. This is a descriptive contrast in the specified randomized groups and time window. It does not tell how many bleeds occurred among participants who had a nonzero rate, nor does it characterize bleeding outside the stated interval.

The statistical interpretation is complicated by the disagreement between the registry’s primary analysis and a simple unadjusted recalculation. The registry’s own confidence interval spans zero, whereas the recalculation’s interval excludes zero. Because the discrepancy is flagged, the sponsor’s analysis takes precedence. The recalculation should be understood as a check on the posted summaries, not as a reason to disregard the sponsor-reported result.

Neither the percentages nor the statistical tests, on their own, establish that one regimen is clinically preferable. Statistical evidence is not a substitute for considering the size and precision of an estimate, the outcome definition, safety, and the limits of the trial record. No medical advice follows from these registry results.

The results also do not automatically generalize to people or settings outside the studied population, to different dosing targets, or to outcomes over a different period. The record does not report detailed participant characteristics needed to assess how closely the study population resembles other clinical populations. It also does not supply enough detail to judge the effects of missing outcomes or the full multiplicity plan.

In short, the record documents group percentages and a disagreement in inferential results. It supports describing the observed pattern, but not a stronger claim than the registry’s analysis and its limitations allow.

18. Why This Trial Matters Statistically

This trial illustrates why it is important to separate an observed group difference from the statistical analysis used to assess it. The primary percentages are straightforward to describe, but the sponsor-reported interval and a simple recalculation lead to different conclusions about whether the contrast is distinguishable from zero. A reader who sees only the group percentages could miss that important uncertainty about the inferential result.

It also demonstrates why the analysis population and endpoint definition matter. The primary outcome concerns the proportion with zero annualized bleeding during one defined period. The secondary mean bleeding rates describe a different feature of the data. Agreement in direction across these summaries is useful context, but it does not make them equivalent or eliminate the need to account for multiple outcomes.

The record gives enough detail to identify the two dosing targets, the primary time window, the analysis population definition, and the sponsor’s reported test. At the same time, it leaves important statistical questions unanswered, including the original sample-size justification, missing-data procedures, and multiplicity handling. This combination makes the study a useful example of how registry summaries can support careful description while leaving aspects of the analysis difficult to reconstruct.

Finally, the sample-size illustrations show how planning depends on the effect chosen for detection. They are not a substitute for the original design rationale, and they are not observed power. Treating planning calculations, sponsor analyses, and recalculated summaries as distinct forms of evidence helps avoid overstating what the registry record establishes.

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 study was open label, so participants and study personnel were not masked according to the registry. The record does not explain whether knowledge of the assigned dosing target could have influenced event recording or other study procedures. This is a design feature to consider when interpreting a bleeding outcome recorded during follow-up.

The primary endpoint is limited to Day 183 to Day 364. It does not summarize the full study duration, and annualization relies on the observation period in years. The registry does not provide details on how incomplete observation periods or missing bleed records were handled. The primary analysis population includes randomized participants treated prophylactically for any period, but that definition alone does not resolve possible missing-data concerns.

The primary inferential results are discrepant: the sponsor-reported interval spans zero, while the unadjusted recalculation’s interval excludes zero. The record does not explain why. The sponsor analysis takes precedence, but the absence of sufficient methodological detail limits independent reconstruction of that result.

There are also multiple secondary outcomes, while multiplicity handling is not reported. The listed secondary comparisons are unadjusted, and numerical results for the other secondary endpoints are not reported in the registry record. The mean and standard deviation summaries do not reveal the distribution of individual bleeding rates, and the record does not describe whether the secondary outcomes were modeled to account for the characteristics of event-count data.

Participant characteristics, detailed eligibility criteria, the original sample-size justification, and missing-data sensitivity analyses are not reported in the registry record. These omissions limit assessment of generalizability, design assumptions, and robustness.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BAX 855 PK-guided Dosing — NCT02585960.
• Registry record last updated 2021-05-25; status last verified 2021-05.
• Results first posted 2019-08-26.
• 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

NCT02585960 is a completed phase 3, prospective, randomized, open-label, parallel-group study of pharmacokinetic-guided BAX 855 prophylaxis in severe hemophilia A. It compared target FVIII trough levels of 1-3% and 8-12%. Enrollment was 135; the study start date was 2015-11-23, and primary completion was 2018-08-05.

The primary endpoint was the percentage with a total annualized bleeding rate of zero from Day 183 to Day 364. The posted percentages were 42.1% in the low-level group and 62.1% in the high-level group. The sponsor-reported primary analysis and an unadjusted recalculation differ; the sponsor’s own analysis takes precedence. The record does not report the original sample-size justification, missing-data methods, or multiplicity procedure.