Prophylaxis Study of Recombinant Factor VIII Manufactured Protein-Free (rAHF-PFM) in Patients With Hemophilia A: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prophylaxis Study of Recombinant Factor VIII Manufactured Protein-Free (rAHF-PFM) in Patients With Hemophilia A (NCT00243386), a randomized phase 4 study. The primary outcome is Mean Transformed Annualized Bleed Rate Estimates From Each of the 1-year Prophylaxis Regimens.

2. Clinical Question

The trial compared two active prophylactic schedules rather than prophylaxis with no treatment. Its central statistical question was whether the observed mean transformed bleeding rate differed between the PK-driven and standard regimens in the per-protocol analysis. The posted group means were 1.61 for PK-driven prophylaxis and 1.46 for standard prophylaxis, in the transformed units stated for the endpoint. The recalculated unadjusted mean difference was 0.15, with the PK-driven group higher on this transformed scale.

This is a comparison of group averages, not a direct statement about the experience of every participant. The endpoint applies a transformation to annualized bleeding rates, so a difference in transformed means should not be read as a simple difference in the number of bleeding episodes per year. The clinical question also sits within a broader study sequence: the brief summary describes an initial on-demand period followed by random assignment to one of the prophylaxis regimens, and describes comparisons involving the on-demand period as well. The primary posted outcome, however, is the comparison between the two prophylaxis arms.

The record identifies the study as randomized, with two parallel arms and no masking. It does not report a formal non-inferiority or equivalence objective for this primary comparison. Accordingly, the result is best read as an estimate of the difference between the assigned prophylactic schedules, with the uncertainty represented in the accompanying confidence interval, rather than as a test that one regimen was established to be equivalent to the other.

3. Trial Design

This was a phase 4, randomized, parallel-group study of recombinant factor VIII manufactured protein-free in people with severe or moderately severe hemophilia A. The record lists 82 participants enrolled. Its brief description says the primary purpose was to compare bleeding-episode rates for standard and alternate prophylaxis in 66 previously treated patients. It also describes an on-demand period before randomization, followed by prophylactic treatment for 12 months ± 2 weeks. The primary outcome timeframe is likewise recorded as 12 months ± 2 weeks.

The two groups received the same named product but different schedules. Standard prophylaxis was described as 20-40 IU/kg every 48 ± 6 hours, with the investigator determining the exact regimen. PK-driven prophylaxis was described as 20-80 IU/kg every 72 ± 6 hours, with the sponsor determining the exact regimen using an algorithm and pharmacokinetic data. The registry identifies the allocation as randomized and the model as parallel. Masking was listed as none, so the record does not describe a masked comparison.

The main outcome analysis used the per-protocol population. The posted group sizes for that endpoint were 23 for PK-driven prophylaxis and 30 for standard prophylaxis. The total enrolled count and the brief description’s count of previously treated patients do not match the primary-analysis group sizes; the registry record does not explain participant flow, exclusions, or the reasons for the difference. It also does not report a detailed account of adherence, treatment discontinuation, or missing endpoint data in the registry record.

The brief summary describes comparisons of bleeding rates during the on-demand and prophylaxis periods as part of the study, including a cross-over portion. The posted primary result is specifically the comparison between the two prophylaxis regimens. The original sample-size justification, design assumptions, and any interim analyses are not reported in the registry record. The planning illustrations discussed elsewhere on this page are separate calculations based on the observed effect, not the trial’s original design plan.

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: 82 participants were enrolled and screened. 7 were screen failures, 1 was withdrawn for non-compliance, and 1 requested withdrawal. Therefore, 73 of the 82 enrolled were exposed to investigational product in the first part of the study (on-demand treatment).

On-Demand Regimen (Study Part 1)

Reasons for not completing this period:

End of Part 1, But Prior to Prophylaxis

Reasons for not completing this period:

PK-Driven or Standard Prophylaxis

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol

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 Mean Transformed Annualized Bleed Rate Estimates From Each of the 1-year Prophylaxis Regimens, measured over 12 months ±2 weeks.

The primary endpoint is the mean transformed annualized bleed rate estimate for each one-year prophylaxis regimen. Annualized bleeding rate represents bleeding episodes expressed on a yearly scale. For this analysis, the registry says the rate was transformed using the square root of the number of bleeding episodes observed, with 0.5 added before taking the square root: X' = √(X + 0.5). The endpoint unit is recorded as (bleeds/year)^(1/2), and its timeframe is 12 months ± 2 weeks.

The transformation is used to make the distribution more suitable for a method that compares means. The registry description says it was intended to stabilize variance and align the sample distribution with the normality assumption inherent in the t-test. In general, count outcomes can be unevenly distributed, particularly when many observations are low and some are much higher. A transformation can reduce the influence of that unevenness, although the analysis then concerns transformed rates rather than the original rate scale.

The reported endpoint is a group mean with standard deviation. This summarizes the central value and the spread of transformed annualized rates within each analysis group. It does not show the full distribution, the number of participants with no bleeding episodes, or how many episodes each individual experienced. Those details are not reported in the registry record. The transformed mean difference is therefore most directly interpreted on the stated transformed scale; it should not be converted into an untransformed difference in bleeds per year without participant-level information and an appropriate analysis.

Using a common endpoint definition for both arms allows a direct comparison of the assigned prophylaxis regimens. The transformation and the t-test are methodological choices, not evidence in themselves that the regimens differ. The observed group estimates and the uncertainty around their contrast carry the information relevant to the comparison.

7. Results Posted in the Registry

• PK-Driven Prophylaxis: mean 1.61 versus 1.46 on control; difference 0.15 (95% CI -0.42 to 0.72), standardized effect d = 0.15; z-test p = 0.606.

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 Who Reported ≥1 AE Regardless of Relatedness to IP by Treatment Regimen

• 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:
  • On-Demand: 45.8% (33/72) versus 46.9% (15/32) on control; risk difference -1.0 percentage points (95% CI -21.8 to 19.7), risk ratio 0.98 (0.63–1.53); unadjusted two-proportion z-test p = 0.922.
  • PK-Driven Prophylaxis: 55.9% (19/34) versus 46.9% (15/32) on control; risk difference 9.0 percentage points (95% CI -15.0 to 33.0), risk ratio 1.19 (0.74–1.92); unadjusted two-proportion z-test p = 0.464.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between On-Demand and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PK-Driven Prophylaxis and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including comparisons of transformed annualized bleeding rates across on-demand and prophylaxis periods, dose use, treatment of bleeding episodes, hemostasis assessments, and area-under-the-curve measures. It also records a secondary endpoint counting participants with at least one adverse event regardless of relatedness to the investigational product. These outcomes address different questions and use different kinds of measurements; they should not be treated as interchangeable confirmations of the primary endpoint.

The summarized secondary information does not establish a consistent direction of effect across all secondary outcomes. The available results include an adverse-event count comparison, while estimates or test results for many other listed outcomes are not reported in the registry record. A pattern across the whole secondary-outcome set therefore cannot be confidently characterized from these summaries alone. The calculated tables should be used to inspect the individual posted results, while recognizing that an absent result is not evidence of no difference.

These analyses relate to the primary result by adding context about other aspects of the study, but they do not answer the primary question more directly than the randomized comparison of transformed annualized bleeding rates. The on-demand comparisons, in particular, involve a different treatment period and study sequence from the primary comparison between the two prophylaxis arms. The registry does not report enough detail to assess all dependencies among those measurements or how each analysis handled repeated observations.

Unadjusted secondary results generally carry less inferential weight when many outcomes or comparisons are examined. In general, testing many hypotheses without a specified adjustment or hierarchy increases the possibility that some results appear noteworthy by chance. The record notes 29 outcome measures and 9 analyses, and 26 secondary outcomes are posted, but the registry entries do not identify a multiplicity correction or a prespecified hierarchy for interpreting them. Secondary findings are therefore best viewed as supportive or exploratory unless the registry record provides a clear analysis plan and confirmatory framework.

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

• Mean Difference of Transformed Annualized Bleeding Rate Between On-Demand and Standard Prophylaxis Treatment Regimens
• Mean Difference of Transformed Annualized Bleeding Rate Between On-Demand and PK-Driven Prophylaxis Treatment Regimens
• Mean Difference of Transformed Annualized Bleeding Rate Between On-Demand and Any Prophylaxis Treatment Regimens
• Total Weight-Adjusted Dose of rAHF-PFM Used Per Year for Each Prophylaxis Arm
• Bleeding Episodes Treated With 1 to ≥4 Infusions
• Assessment of Hemostasis for Treatment of Bleeding Episodes
• Total Area Under the Curve (AUC)
• Area Under the Curve

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous after transformation, and the registry reports a mean and standard deviation for each prophylaxis arm. A two-sided t-test is listed in the sponsor’s reported analysis. The calculated recalculation uses the posted group summaries to estimate the unadjusted difference between the means and its confidence interval. These are two related presentations of the same basic comparison, but a recalculation from summary statistics is not necessarily identical to the sponsor’s original analysis procedure.

Why transform the bleeding rate?

Annualized bleeding rate is based on counts of bleeding episodes. Count outcomes may be skewed: many participants can have relatively low counts, while a smaller number have larger counts. A standard mean-based analysis works most naturally when the residual distribution is reasonably compatible with its assumptions and the variability is manageable. The registry states that the square-root transformation was used to stabilize variance and align the sample distribution with the normality assumption inherent in the t-test. The transformation adds 0.5 to the rate before taking its square root, as described in the endpoint definition.

In general, transformation changes the scale on which a comparison is made. It can make a distribution more suitable for a statistical method, but it also means that the estimated difference is not directly expressed in the original clinical units. The transformed group means are therefore interpreted as means of transformed annualized rates. The registry does not report a separate model on the untransformed count scale in the registry record.

What does the t-test compare?

A two-sample t-test compares the group means, using the observed variation and sample sizes to quantify uncertainty. A two-sided test considers departures in either direction: the PK-driven mean could be higher or lower than the standard-prophylaxis mean. The sponsor’s reported analysis is described as a two-sided t-test. The recalculated result is an unadjusted comparison based on the posted means, standard deviations, and analysis-group sizes. The term unadjusted means that the recalculation does not incorporate additional covariates or a multiplicity correction.

A t-test does not require the two groups to have exactly identical distributions, but its inference relies on assumptions about the sampling process and the behavior of the mean. With modest group sizes, unusual distributions or influential observations can matter. The transformation was intended to support the normality assumption, but the registry record does not provide diagnostic plots, participant-level data, or a description of checks for outliers or residual behavior. Those aspects therefore cannot be evaluated from the posted summary statistics alone.

How should the estimate and p-value be read?

The estimated mean difference is 0.15 on the transformed scale, with the PK-driven arm as the first group in the subtraction. The unadjusted p-value is 0.606. In general, a p-value measures how unusual a result at least as extreme as the observed one would be under a specified null hypothesis and statistical model. It is not a measure of the size or clinical importance of an effect, and it is not the probability that a result is due to chance. The estimated difference and confidence interval are more informative about direction, magnitude, and precision than the p-value alone.

The analysis population is per protocol. In general, a per-protocol analysis includes participants meeting specified criteria for following the study protocol; the criteria themselves are not reported in the registry record. Such an analysis can be informative about outcomes among participants included in that set, but it may not preserve all the advantages of random assignment if inclusion depends on events after randomization. The registry does not provide enough detail to assess the criteria or compare the per-protocol result with an intention-to-treat analysis. An intention-to-treat result is not reported in the registry record.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It matters especially for count outcomes because a model that understates variability can produce confidence intervals that are too narrow and p-values that are too small. Transforming rates and using a t-test is one approach to handling distributional concerns, but it does not demonstrate that all assumptions are satisfied. The registry gives the rationale for the transformation but does not report a formal assessment of over-dispersion or a comparison of alternative count models.

For this endpoint, the posted standard deviations describe variability on the transformed scale, and the t-test uses that variability to assess the mean contrast. The numerical summaries do not show whether variability differed by participant characteristics, whether repeated measurements were modeled, or how within-person correlation was handled in any broader longitudinal analysis. These details are not reported in the registry record. The simple recalculation should therefore be understood as a summary-statistic comparison, not a reconstruction of every feature of the sponsor’s analysis.

Finally, the study includes multiple outcomes and comparisons. Each unadjusted test is evaluated on its own. If many tests are performed, the chance of at least one apparently notable result can rise, in general, unless a multiplicity strategy is specified. The registry entries do not identify a multiplicity adjustment or a prespecified testing hierarchy. The primary comparison should consequently be distinguished from secondary and exploratory findings, which may carry less inferential weight.

11. Confidence Intervals and Precision

The recalculated confidence interval for the primary mean difference spans from a negative value to a positive value, crossing zero. This means the posted summary data are compatible with no mean difference as well as with differences in either direction. The interval is wide relative to the estimated difference of 0.15, so the estimate is not very precise. The tables and plot display the interval numerically; the important interpretive point is that they do not confine plausible values to one direction.

In general, a confidence interval is a range produced by a procedure that, under its assumptions and repeated use, would cover the true parameter at the stated rate. It is not a range containing a known probability that the true value lies within it after the data have been observed. Nor does an interval crossing zero prove the absence of an effect. It shows that the estimate remains uncertain and that the data do not sharply distinguish between zero and some nonzero differences.

Precision depends on the size of the observed effect, the variability of outcomes, and the number of participants contributing to the analysis. Here, the per-protocol groups included 23 and 30 participants, and the reported standard deviations were 1.1 and 0.98. The observed mean contrast is modest relative to the spread in transformed values. Together, these features help explain why the interval is broad. They do not establish whether a particular difference would be clinically important; the registry record does not report a threshold for clinical importance.

The confidence interval is for the mean difference on the transformed scale. Its limits should not be interpreted as limits for an untransformed difference in bleeding episodes per year. The interval also reflects the assumptions of the recalculated method and does not incorporate unreported design features or adjustments. The sponsor’s own analysis should be considered separately, as discussed in the sponsor reading. The interval is useful for showing uncertainty, but it cannot resolve questions about missing outcomes, analysis-population selection, or clinical importance that are not answered in the registry record.

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 table and curve are planning illustrations based on the observed effect, not the trial’s original design justification. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show the participants per arm needed to detect the stated portion of the observed effect under those assumptions. These figures are per arm, not totals, for the comparisons.

The 80% power column describes a planning scenario in which a study of the stated size would have an 80% chance of detecting the assumed effect using the specified test, if that effect and the calculation assumptions were correct. The 90% power column describes the corresponding scenario with a 90% chance. These are prospective planning concepts. They are not measures of how likely this completed trial was to find a result after observing its data, and this is not observed power.

The rows show planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. Under the stated assumptions, planning to detect a smaller effect requires more participants. This is why the participant requirements increase as the assumed effect becomes smaller. The values are illustrations rather than recommendations: they inherit uncertainty from the observed effect and do not account for features not included in the stated assumptions.

The original protocol’s sample-size assumptions, including its target effect and any allowance for attrition, are not reported in the registry record. The planning figures should not be used to infer what the trial was designed to detect, or to label the completed comparison adequately or inadequately powered. The curve provides a visual presentation of the same planning relationship as the table; it does not add an independent analysis of the observed trial result.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.150; pooled standard deviation σ = 1.033.
2. n = 2 × (1.96 + 0.842)² × 1.033² / 0.150² = 745.2, rounded up to 746 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
delta <- 0.15                      # observed difference in means
sigma <- 1.03347500610092                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(243386)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 746 (80% power), 998 (90% power)
 75% of observed effect: n per arm = 1,325 (80% power), 1,774 (90% power)
 50% of observed effect: n per arm = 2,981 (80% power), 3,991 (90% power)
power.t.test: 746.1 
Simulated power at n = 746 per arm: 0.803 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 reports that the sponsor used a two-sided t-test for the primary comparison and gives a p-value of 0.602. The summary-statistic recalculation gives an unadjusted p-value of 0.606, alongside a recalculated mean difference and confidence interval. The p-values are close, but they are not identical. The recalculation is based on posted group summaries, whereas the sponsor’s own analysis is the reported trial analysis. The registry record does not explain the small difference between the two p-values, so no specific cause should be inferred.

The sponsor’s entry does not report a primary mean-difference estimate or confidence limits in the registry record. Those are presented by the calculated recalculation from the posted arm-level means, standard deviations, and group sizes. They should be read as simple unadjusted re-calculations, not as replacements for a fuller sponsor analysis. Because the discrepancy indicator is false, the registry entries do not identify a substantive conflict requiring the recalculation to displace the sponsor’s result.

Both reported and recalculated p-values are consistent with the general interpretation that the primary comparison does not provide clear evidence of a difference under the two-sided test. Neither p-value establishes equivalence or proves that the regimens have the same mean outcome. The recalculated confidence interval adds a direct view of the uncertainty around the estimated difference, while the sponsor’s reported analysis remains the source for the trial’s stated test result.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, treatment contrasts, time points, or analysis populations. In general, the more statistical tests performed, the greater the chance that at least one will produce an apparently unusual result even if there is no underlying effect for that particular comparison. Researchers can address this by defining a primary endpoint, setting a testing hierarchy, adjusting significance thresholds, or treating secondary analyses as exploratory. The registry entries identify a primary outcome and list many secondary outcomes, but do not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary tests.

The record lists 29 outcome measures and 9 analyses, with 26 secondary outcomes posted. These counts indicate that the study reported multiple assessments, but they do not by themselves tell us how many distinct hypotheses were formally tested or how those tests were planned. The registry record does not report the original statistical analysis plan, whether secondary outcomes were prespecified in a particular order, or whether any multiplicity procedure was used. Consequently, isolated secondary p-values should not be treated as definitive evidence without more detail.

Missing-data handling is another important issue. The primary result is reported for a per-protocol population, but the registry entries do not describe the protocol criteria, how many participants were excluded from that analysis, the reasons for exclusion, or how missing outcome measurements were handled. The relationship between total enrollment, the brief description’s count of previously treated patients, and the primary-analysis group sizes is not explained in the registry record. No intention-to-treat estimate is reported in the registry record.

In general, analysis-population choices can influence a treatment comparison if inclusion depends on events after randomization. Random assignment helps balance groups at baseline, but exclusions after assignment can weaken that protection. Without participant flow, missing-data methods, and results for other analysis populations, it is not possible to determine how sensitive the primary estimate is to these choices. These omissions limit the assessment of robustness; they do not justify assuming that missing observations favored either regimen.

The registry does not report interim analyses or the trial’s original sample-size assumptions. Those details matter for understanding how the study’s design and analysis were coordinated, but they cannot be reconstructed from the posted outcome summaries. The absence of reporting should be distinguished from evidence that a procedure was or was not used.

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: pain in extremity (100.0%), pulpitis dental (3.1%), somnambulism (3.1%), haemophilic arthropathy (2.9%), factor viii inhibition (2.9%).

The safety summary lists participants at risk and participants affected by serious adverse events separately for on-demand, standard-prophylaxis, and PK-driven-prophylaxis groups, as well as a category for serious adverse events outside the three treatment arms. The accompanying table should be read by keeping each treatment group and its stated at-risk count in view. The counts describe participants with at least one event in the specified category; they do not describe the total number of event episodes or establish that an event was caused by treatment.

The registry also lists terms among the serious adverse events, including pain in extremity and several other event terms. Such terms are descriptive classifications, not evidence of a causal relationship. The summary does not provide enough context to evaluate timing, severity details, recurrence, clinical course, or attribution for each event. The record lists deaths as not reported in the summarized safety data; it does not support an inference about mortality beyond that reporting status.

Comparisons of safety counts should be interpreted cautiously because the groups differ in size and the study includes different treatment periods. The record does not provide a randomized, concurrent comparison for every safety category described. The table is a descriptive account of reported serious events, not a formal demonstration that one schedule is safer than another. It should be considered alongside the study’s design and the limits of the posted safety information.

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

The primary result means that, among participants included in the per-protocol analysis, the observed mean transformed annualized bleeding-rate estimate was 1.61 for PK-driven prophylaxis and 1.46 for standard prophylaxis. The recalculated difference was 0.15 in the direction of a higher transformed mean in the PK-driven group. The confidence interval crosses zero and is broad, so the result leaves considerable uncertainty about the size and direction of the underlying difference.

The result does not show that the two regimens are equivalent. Failure to find clear evidence of a difference is not the same as evidence that any difference is small enough to be unimportant. Equivalence or non-inferiority requires an appropriate prespecified objective, margin, and analysis. Those are not reported in the registry record. Nor does the result show that either regimen works or does not work; the comparison is between two active prophylaxis schedules, and the statistical summary describes their relative outcomes on a transformed endpoint.

The mean difference is not an untransformed difference in annual bleeding episodes. It is a contrast between means after the specified square-root transformation. The summary also cannot show how outcomes varied for individual participants, whether a small number of participants contributed unusually high rates, or the proportion with particular patterns of bleeding. Those details are not reported in the registry record.

The trial’s findings are specific to the population and analysis represented in the record: previously treated people with severe or moderately severe hemophilia A, analyzed per protocol for the primary endpoint. Total enrollment was 82, but the primary analysis groups were smaller; the record does not explain the full participant flow. The absence of masking and the lack of detail about missing data and analysis-population criteria are further reasons to avoid extending the result beyond what the posted analysis supports.

In practical statistical terms, the estimate is compatible with a range of possible differences, not a definitive ranking. The posted data do not establish a clinically important difference, and the registry does not report a threshold for clinical importance. Interpretation should therefore remain focused on the estimated contrast, its uncertainty, and the limits of the available record rather than on a binary claim of success or failure.

18. Why This Trial Matters Statistically

This study illustrates why an estimate and its precision should be read together. The point estimate alone suggests a small difference in mean transformed annualized bleeding rate, but the confidence interval is broad and crosses zero. Reporting only the p-value would conceal the range of effects still compatible with the data; reporting only the group means would omit uncertainty. The calculated table and plot help make both features visible.

It also shows how the scale of an endpoint shapes interpretation. Bleeding rates begin as counts expressed on an annualized scale, but the primary analysis uses a square-root transformation. That choice was intended to support a mean-based t-test by stabilizing variance and aligning the distribution with a normality assumption. In return, the treatment contrast is expressed on a transformed scale, which is not immediately interpretable as a difference in raw bleeding episodes.

The study also highlights the distinction between a trial’s original design and a later planning illustration. Calculations based on the observed effect can show how assumptions about effect size relate to participant requirements, but they do not reveal the original design target or establish whether the completed study had adequate power. The original sample-size rationale is not reported in the registry record. Keeping those concepts separate prevents retrospective planning calculations from being mistaken for evidence about the trial’s design.

Finally, the record makes clear that a primary endpoint does not exist in isolation. The study includes numerous secondary outcomes, a per-protocol primary analysis, and safety summaries across treatment periods. Without a reported multiplicity strategy, participant flow, and missing-data methods, readers have to distinguish the most direct randomized comparison from less definitive secondary findings. This is a useful example of how statistical interpretation depends not just on a numerical result, but also on the analysis population, endpoint scale, and completeness of reporting.

19. Limitations

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

The primary estimate is based on the per-protocol population, with 23 participants in the PK-driven arm and 30 in the standard arm. The registry record does not describe the criteria for inclusion in this population or report an intention-to-treat result. The full participant flow and reasons why the primary analysis groups are smaller than total enrollment are also not reported. This limits assessment of how selection into the analysis may have affected the comparison.

The endpoint is analyzed after a square-root transformation. That choice has a stated statistical rationale, but it makes the mean difference less directly interpretable in the original scale of bleeding episodes. The registry summary does not provide participant-level distributions, alternative count-model results, or enough detail to evaluate the transformation’s fit. It also does not report a threshold for a clinically important difference, so statistical uncertainty cannot be translated into a judgment about clinical importance from this record alone.

The study was randomized and parallel, but masking was listed as none. The record does not report how outcome ascertainment was standardized, whether bleeding episodes were independently adjudicated, or how assessment might have been affected by knowledge of treatment. These details should not be guessed. The summary also does not give detailed adherence, discontinuation, or missing-outcome information.

The record describes secondary comparisons involving the on-demand period, as well as multiple other outcomes, but does not report a multiplicity strategy or a full hierarchy for interpreting them. This limits the confirmatory weight that can be placed on individual secondary findings. Safety summaries are descriptive and include categories outside the three treatment arms, so they are not a clean basis for causal comparisons of safety.

Finally, the registry does not report the original sample-size justification, interim analyses, or a detailed statistical analysis plan in the registry record. The recalculated results use posted aggregate statistics and cannot reproduce analyses that require participant-level data or unreported modeling choices. These limitations concern the scope and precision of interpretation; they do not establish that the reported result is biased in a particular direction.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Prophylaxis Study of Recombinant Factor VIII Manufactured Protein-Free (rAHF-PFM) in Patients With Hemophilia A — NCT00243386.
• Registry record last updated 2021-05-19; status last verified 2021-04.
• Results first posted 2012-11-20.
• 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

This completed phase 4 study compared standard and PK-driven prophylaxis with recombinant factor VIII manufactured protein-free in people with severe or moderately severe hemophilia A. It was randomized, parallel-group, and unmasked. The primary endpoint was the mean transformed annualized bleeding-rate estimate over 12 months ± 2 weeks, analyzed in the per-protocol population.

The posted means were 1.61 for PK-driven prophylaxis and 1.46 for standard prophylaxis. The recalculated unadjusted mean difference was 0.15, with uncertainty that includes zero. The registry reports a two-sided t-test for the sponsor’s analysis. The primary result does not establish equivalence or a clinically important difference.

The registry describes an initial on-demand period, multiple secondary outcomes, and safety events across treatment groups and periods. Details about missing data, participant flow, multiplicity handling, the original sample-size rationale, and interim analyses are not reported in the registry record.