Hokusai Study in Pediatric Patients With Confirmed Venous Thromboembolism (VTE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hokusai Study in Pediatric Patients With Confirmed Venous Thromboembolism (VTE) (NCT02798471), a randomized phase 3 study. The primary outcome is Number of Participants With Symptomatic Recurrent Venous Thromboembolism During the Main Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite).

2. Clinical Question

The study is described as an event-driven Phase 3 trial in pediatric participants with confirmed VTE. Its primary efficacy outcome is a count of participants experiencing a defined event, rather than a continuous measurement. The registry record reports the two group counts and a sponsor-reported Cox analysis, as well as a simple unadjusted recalculation of the difference in event proportions. Those analyses summarize the same trial but use different effect measures and should not be treated as interchangeable.

3. Trial Design

The registry describes a Phase 3, randomized, parallel-group, multicenter, open-label trial with blinded endpoint evaluation. The brief summary calls the design PROBE: prospective, randomized, open-label, blinded endpoint evaluation. The record lists single masking, but does not identify in the posted record who was masked. Participants were assigned to edoxaban or standard of care, and the registered enrollment was 290.

The registered population was pediatric subjects from birth to less than 18 years of age with confirmed VTE. The trial began on 2017-03-27, reached primary completion on 2022-05-24, and is listed as completed. The registry record describes the study as event-driven, but does not report the event target or the operational rules used to determine when enrollment or follow-up would stop.

The primary endpoint was assessed from randomization to Month 3 in the modified intent-to-treat population. The posted arm counts for this endpoint are 5 participants among 145 in the edoxaban group and 2 among 141 in the standard-of-care group. These analysis counts are not the same as the registered enrollment figure; the registry record does not explain that difference in the endpoint results presented.

Monthly dispensing visits are described for both groups. The edoxaban arm description says treatment would be oral and dosed according to age, weight, and renal function, with the dose depending on results from an ongoing study. The posted description does not give a complete dose regimen, and the standard-of-care arm description does not name specific anticoagulants. The record also lists pharmacokinetic and pharmacodynamic evaluation as study aims, alongside efficacy and safety comparisons.

The registry record does not report the original sample-size justification, the planned event target, the detailed randomization procedure, or the specific endpoint-masking process. These details should not be inferred from the randomized or blinded-endpoint labels alone.

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: Symptomatic recurrent VTE was assessed in the modified intent-to-treat population (mITT).

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: Baseline demographic characteristics were reported in the Randomized Analysis Set.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Symptomatic Recurrent Venous Thromboembolism During the Main Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite), measured over Randomization to Month 3.

The primary endpoint counts participants with symptomatic recurrent venous thromboembolism during the main treatment period, defined as randomization to Month 3. It is an adjudicated composite: recurrent VTE required confirmation by diagnostic imaging and at least one symptom of VTE. The registry description includes events involving the lower or upper extremity, catheter-related thrombosis, pulmonary embolism, or sinovenous thrombosis.

A participant count is a binary outcome at the participant level: each person is classified according to whether the defined event occurred during the specified period. This makes the result directly readable as the number of participants with an event in each randomized group. It does not describe the total number of recurrent episodes if a participant could experience more than one event; such episode-level information is not reported for this endpoint.

General statistical context: a prespecified clinical endpoint provides a consistent rule for deciding which observations count as outcomes. Adjudication can help apply that rule consistently, particularly when event classification depends on diagnostic evidence and symptoms. A composite combines more than one type of event under a single outcome definition, so the overall count does not by itself show how often each component occurred. The registry lists some related component outcomes among its secondary measures, but the primary result is the composite count for the main treatment period.

The endpoint is clinically relevant to the study question because the trial aims to compare efficacy and safety of edoxaban with standard-of-care anticoagulant therapy in children with confirmed VTE. Its short stated timeframe is important when interpreting it: the primary result concerns events through Month 3, not the longer overall treatment period.

7. Results Posted in the Registry

• Edoxaban: 3.4% (5/145) versus 1.4% (2/141) on control; risk difference 2.0 percentage points (95% CI -1.5 to 5.6), risk ratio 2.43 (0.48–12.33); unadjusted two-proportion z-test p = 0.267.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With Symptomatic Recurrent Venous Thromboembolism During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)

• 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:
  • Edoxaban: 4.8% (7/145) versus 1.4% (2/141) on control; risk difference 3.4 percentage points (95% CI -0.6 to 7.4), risk ratio 3.40 (0.72–16.10); unadjusted two-proportion z-test p = 0.099.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Edoxaban and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With No Change or Extension of Thrombotic Burden During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)

• 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:
  • Edoxaban: 24.1% (35/145) versus 33.3% (47/141) on control; risk difference -9.2 percentage points (95% CI -19.6 to 1.2), risk ratio 0.72 (0.50–1.05); unadjusted two-proportion z-test p = 0.086.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Edoxaban and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Major and Clinically Relevant Non-Major Bleeding Events (On Treatment) During the Main Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)

• 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:
  • Edoxaban: 2.1% (3/145) versus 3.5% (5/141) on control; risk difference -1.5 percentage points (95% CI -5.3 to 2.4), risk ratio 0.58 (0.14–2.40); unadjusted two-proportion z-test p = 0.449.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Edoxaban and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend the assessment beyond the primary endpoint period and include recurrent VTE, thrombotic burden, bleeding, mortality, and other VTE event categories. Across these outcomes, the observed counts and unadjusted comparisons vary; the registry record does not present a single common pattern that can be treated as a comprehensive summary of efficacy or safety. The outcomes also differ in definition and timeframe, so their estimates should be read within their own endpoint descriptions.

These secondary findings provide context for the primary result but do not replace it. The primary endpoint concerns adjudicated symptomatic recurrence during randomization to Month 3. Some secondary measures cover the overall treatment period up to Month 12, while others concern distinct events or composites. A difference in an outcome over a longer period is not a direct confirmation or contradiction of the primary-period estimate.

General statistical context: when many outcomes are examined, the chance of at least one apparently notable result can increase, even if the underlying effects are absent. Unadjusted secondary results do not account for the number of comparisons and should therefore carry less weight than a prespecified primary analysis. The registry record does not report a multiplicity adjustment strategy or a hierarchy for interpreting the secondary endpoints. Accordingly, secondary p-values and interval estimates are best treated as exploratory evidence rather than as independent confirmatory findings.

The endpoint list also includes outcomes with related or overlapping clinical content. Without a reported multiplicity plan and complete analysis details, the results should not be combined informally into a single conclusion. Their main value is to describe additional outcomes recorded during follow-up and to identify areas where further evidence could be useful, while recognizing that the number of events is limited for several measures.

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

• Number of Participants With Symptomatic Recurrent Venous Thromboembolism During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)
• Number of Participants With Symptomatic Recurrent VTE During the Main Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Individual Component of Primary Efficacy Endpoint)
• Number of Participants Who Died as a Result of VTE During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)
• Number of Participants Who Died as a Result of VTE During the Main Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Individual Component of Primary Efficacy Endpoint)
• Number of Participants With No Change or Extension of Thrombotic Burden During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated Composite)
• Number of Participants With Adjudicated Individual Component of Primary Efficacy Endpoints During the Main Treatment Period Following Edoxaban or Standard of Care Treatment
• Number of Participants Reporting Adjudicated All-Cause Mortality During the Overall Treatment Period Following Edoxaban or Standard of Care Treatment (Adjudicated)
• Number of Participants With Deep Vein Thrombosis, Catheter-related Thrombosis, Sino-venous Thrombosis, and Pulmonary Embolism During the Main, Extension, and Overall Treatment Periods Following Edoxaban or Standard of Care Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The registry record presents a participant-count endpoint and a sponsor-reported Cox regression analysis. The posted primary endpoint counts 5 participants with symptomatic recurrent VTE among 145 in the edoxaban arm and 2 among 141 in the standard-of-care arm. A separate unadjusted recalculation summarizes the difference in observed event proportions. The two analyses should be read as distinct statistical summaries of the same comparison.

What does the risk difference express?

General statistical context: the risk difference subtracts one group’s observed event proportion from the other group’s observed event proportion. In this comparison, the stated direction is edoxaban minus standard of care. The recalculated estimate is 0.020, with a 95% confidence interval from -0.015 to 0.056. The estimate is not an adjusted treatment effect; it is a simple comparison calculated from the posted summary counts. It does not incorporate any covariate adjustment or time-to-event modeling.

The risk difference is often straightforward to interpret because it refers to a difference in event proportions over the defined assessment period. However, the primary endpoint has few events, so the estimate is sensitive to the observed counts and its uncertainty is substantial. The confidence interval includes zero and spans values on either side of it. The unadjusted p-value is 0.267. That p-value is not a measure of the size or clinical importance of the difference and should not be read on its own.

What does the Cox analysis measure?

General statistical context: Cox regression is a time-to-event method. It uses the timing of events and the follow-up information available for participants, rather than reducing the comparison only to the proportion with an event by a fixed endpoint. A hazard ratio compares the event rates over time as represented by the model. Its interpretation depends on the model and the time-to-event data; it is not the same quantity as a risk difference.

The registry reports a Cox regression hazard ratio of 1.01, with a 95% confidence interval from 0.594 to 1.719 and p = 0.969. The analysis is labeled non-inferiority. A non-inferiority analysis requires an agreed margin that defines the largest acceptable difference under the chosen measure. That margin, the detailed model specification, and the sponsor’s conclusion are not reported in the registry record. The estimate and its confidence interval therefore cannot, by themselves, be used to verify whether the intended non-inferiority criterion was satisfied.

Why are the two analyses not interchangeable?

The recalculated risk difference summarizes the observed group proportions during the primary endpoint period. The sponsor-reported Cox analysis uses a time-to-event measure. Differences in estimand and analysis method mean the estimates and p-values are not expected to be numerically identical. A reader should identify the analysis before interpreting its estimate, and should give the registered sponsor analysis priority when discussing the trial’s formal analysis. The simple recalculation is useful as a transparent descriptive check of the posted counts, not as a replacement for the trial’s prespecified analysis.

The registry record does not report the complete statistical analysis plan, the covariates used in the Cox model, the handling of censoring, or any assumptions used to support the model. It also does not describe whether there were interim analyses. These omissions limit independent assessment of the sponsor analysis and should not be filled by assuming conventional choices.

What does a confidence interval contribute?

General statistical context: a confidence interval is a range of estimates generated by a procedure that, under its assumptions, has a stated long-run coverage property. For a single trial, it communicates the uncertainty around an estimate; it is not a probability statement that the true effect lies inside the particular interval. The risk-difference interval crosses zero, while the hazard-ratio interval crosses 1. Those reference values represent no difference for the respective measures. Both intervals are compatible with effects in more than one direction.

A confidence interval is also not a substitute for the endpoint definition, analysis population, or study design. Here, the endpoint is adjudicated and assessed in the modified intent-to-treat population, but other analysis details are not reported. The primary result should therefore be read as a bounded, uncertain estimate for the registered endpoint, rather than a definitive statement about all VTE outcomes, all follow-up periods, or every pediatric subgroup.

What do the planning illustrations mean?

The sample-size illustrations use an observed effect and stated assumptions, rather than the trial’s original design assumptions. General statistical context: planning calculations describe how many participants might be required under a specified effect size and statistical framework. They do not indicate how likely a completed trial was to detect an effect after observing its results. Smaller effects generally require more participants to detect under otherwise similar assumptions. The original design justification is not reported in the registry record.

11. Confidence Intervals and Precision

The primary endpoint comparison is based on few observed events: 5 participants in the edoxaban group and 2 in the standard-of-care group. The unadjusted risk difference is 0.020, and its 95% confidence interval ranges from -0.015 to 0.056. Because the interval includes zero, the posted data are compatible with no difference as well as with a difference in either direction. Its range indicates that the point estimate should not be treated as precise.

The sponsor-reported hazard ratio is 1.01, with a 95% confidence interval from 0.594 to 1.719. The interval includes 1, the no-difference reference for a hazard ratio, and covers estimates on either side. It is not appropriate to compare the width of this interval directly with the risk-difference interval: the measures have different scales and arise from different analyses.

General statistical context: confidence intervals summarize sampling uncertainty under the method’s assumptions. A wider interval indicates less precision about the effect estimate, while a narrower interval indicates greater precision. An interval that includes the no-difference value does not prove there is no effect; it indicates that the data and method do not isolate the estimate from that value at the interval’s stated confidence level.

With few endpoint events, the estimates can vary materially with a small change in event counts. The registry record does not report additional subgroup-specific confidence intervals or enough analysis details to assess whether other sources of uncertainty were addressed. Precision should therefore be judged from the posted intervals in the context of the small number of primary events, without treating a point estimate or p-value as conclusive.

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 are planning calculations based on fractions of the observed effect, not a report of the trial’s original design rationale. For the binary participant-count outcomes described by these illustrations, the figures are participants per arm. The stated convention for any time-to-event planning tables is that they give the total number of events. The primary endpoint result is a binary participant count.

The calculations use 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 original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm calculated to provide an 80% chance of detecting the specified effect under those planning assumptions, if the assumed effect and model conditions hold. The 90% power column applies a higher target chance of detection under the same type of assumptions and consequently requires a larger planned sample for a given effect. These percentages describe design calculations, not certainty that a particular trial will yield a statistically significant result.

Rows based on 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the planning requirement. Smaller effects need more participants to detect than larger effects under otherwise similar assumptions. The displayed numbers are illustrations of possible future planning needs using the observed effect as a starting point. This is not observed power; it does not describe the probability that the completed trial detected its actual effect.

The calculations should not be read as evidence that the trial was designed to those sample sizes. The registry record does not report the trial’s original sample-size justification, and the planning illustrations explicitly use the observed effect rather than a reported protocol target.

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 = 0.014; treatment proportion p₁ = 0.034; average p̄ = 0.024.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2179 = 0.4271.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2174 = 0.1830.
4. n = (0.4271 + 0.1830)² / (0.0203)² = 903.4, rounded up to 904 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 <- 0.0141843971631206                          # control proportion
p1 <- 0.0344827586206897                          # 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(2798471)
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 = 904 (80% power), 1,209 (90% power)
 75% of observed effect: n per arm = 1,443 (80% power), 1,932 (90% power)
 50% of observed effect: n per arm = 2,878 (80% power), 3,852 (90% power)
power.prop.test: 903.4 
Simulated power at n = 904 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 sponsor-reported primary analysis is a Cox regression, with a hazard ratio of 1.01, a 95% confidence interval from 0.594 to 1.719, and p = 0.969. It is labeled as a non-inferiority analysis. This is the trial’s reported formal analysis and should be distinguished from the simple unadjusted recalculation of the event proportions.

The recalculated risk difference is 0.020, with a 95% confidence interval from -0.015 to 0.056 and p = 0.267. It is calculated from the posted counts and does not reproduce the sponsor’s time-to-event model. The measures answer related but different questions: one compares proportions over the endpoint period, while the other summarizes time-to-event data through a hazard ratio. Their estimates and p-values are not directly interchangeable.

The registry record does not report the non-inferiority margin, detailed model specification, or sponsor’s narrative conclusion. As a result, the formal non-inferiority finding cannot be independently interpreted from the estimate and label alone. There is no discrepancy flag between the analyses in the registry data, but the recalculation remains descriptive and does not supersede the sponsor-reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and multiple secondary outcomes, but does not report how the trial controlled the risk of false-positive conclusions across those outcomes. A multiplicity strategy might allocate statistical error across endpoints, define an ordered testing sequence, or designate some outcomes as exploratory; the record does not identify such a strategy. The posted unadjusted secondary comparisons should therefore not be interpreted as if each were an isolated confirmatory test.

General statistical context: testing many hypotheses can increase the chance that at least one result appears statistically persuasive by chance. Adjustment or a prespecified testing hierarchy can address that issue, but it can also affect the thresholds or interpretation used for individual outcomes. Because the relevant plan is not reported in the registry record, the secondary results are most cautiously read as descriptive or exploratory. This does not change the numerical results, but it limits how strongly they can support separate conclusions.

The primary endpoint population is identified as modified intent-to-treat. The registry record does not provide the operational definition of that population, the handling of participants with missing endpoint information, or the imputation or censoring procedures used in the analyses. Missing-data amounts and reasons are also not reported in the endpoint information. These details matter because conclusions can depend on who is included and how incomplete follow-up is handled.

The sponsor analysis is described as Cox regression, but the registry record does not report model covariates, censoring rules, or the assumptions used in the analysis. The non-inferiority margin and the full analysis plan are also not reported. The record does not report whether interim analyses occurred. These omissions prevent a full assessment of the prespecified statistical framework, but they should not be treated as evidence that any particular procedure was or was not used.

Overall, the available information identifies the primary endpoint and analysis population and gives the sponsor’s reported result. It does not provide enough detail to evaluate multiplicity control or missing-data handling independently. The secondary analyses consequently have less confirmatory weight, and the primary result should be interpreted with the uncertainty visible in its confidence interval.

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: febrile neutropenia (4.3%), pneumonia (2.8%), thrombocytopenia (2.1%), headache (2.1%), urinary tract infection (2.1%).

The posted safety figures report 44 participants with serious adverse events among 145 at risk in the edoxaban group and 37 among 141 at risk in the standard-of-care group. The figures for participants with other adverse events are 51 among 145 and 46 among 141, respectively. Three deaths are reported in each group. These are counts as recorded in the registry, not adjusted comparisons.

The registry lists febrile neutropenia at 4.3%, pneumonia at 2.8%, thrombocytopenia at 2.1%, headache at 2.1%, urinary tract infection at 2.1%, and vomiting at 1.4% among the top serious adverse event terms. The listed percentages should be read as registry-reported values; the record excerpt does not give further detail about event severity, timing, relatedness, or how participants with multiple events are represented in those terms.

General statistical context: adverse-event counts describe events or affected participants observed during trial follow-up; they do not by themselves establish that a treatment caused an event. The record does not report adjusted safety comparisons or uncertainty intervals for these figures. Interpretation should account for the trial’s size and the descriptive nature of the posted counts, rather than relying on differences in counts alone.

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

The primary result describes adjudicated symptomatic recurrent VTE during randomization to Month 3 among participants in the modified intent-to-treat population. The posted counts are 5 in the edoxaban group and 2 in the standard-of-care group. The unadjusted risk-difference estimate is 0.020, with a 95% confidence interval from -0.015 to 0.056. The sponsor-reported Cox hazard ratio is 1.01, with a 95% confidence interval from 0.594 to 1.719.

These statistics do not establish that the groups are identical. The risk-difference interval includes zero and the hazard-ratio interval includes 1, while both intervals span effects in more than one direction. The estimates are imprecise, in part because few participants had the primary event. A nonsignificant p-value is not proof of no difference, and the point estimates should not be interpreted without their uncertainty.

The sponsor labels the Cox analysis as non-inferiority, but the non-inferiority margin and sponsor’s conclusion are not reported in the registry record. The label alone does not show whether the trial met its non-inferiority criterion. The registry’s unadjusted recalculation is a descriptive summary of posted counts and is not a substitute for the sponsor’s reported analysis.

The findings also do not answer every question about treatment, every VTE event type, or every period of follow-up. The primary result covers the main treatment period through Month 3; some secondary outcomes cover up to Month 12 and use different definitions. The registry record does not provide enough information about multiplicity, missing data, or analysis details to support stronger claims from the collection of secondary results.

These are statistical descriptions of the posted trial results, not medical advice. They should not be used alone to guide an individual treatment decision. The evidence is bounded by the enrolled pediatric population, the endpoints and follow-up described in the registry, and the uncertainty in the estimates.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. The registry reports a time-to-event Cox analysis as its formal primary analysis, while an unadjusted recalculation can express the posted participant counts as a risk difference. Those measures have distinct interpretations and are not interchangeable. A careful reading keeps the sponsor-reported analysis separate from a simpler descriptive calculation.

The example also shows how a small number of endpoint events limits precision. Although an estimate gives a compact summary, the confidence interval communicates that a broad range of effects remains compatible with the observed data. The interval is therefore central to interpretation, not a technical detail to be set aside after reading a point estimate or p-value.

Non-inferiority labels require particular care. A non-inferiority analysis depends on a margin chosen to define an acceptable difference, along with the associated design and analysis plan. When the margin and sponsor’s conclusion are not reported in the registry record, the label and hazard ratio cannot establish the intended decision criterion on their own.

The trial also provides a useful example of how endpoint duration and definition shape the question. Symptomatic recurrent VTE during the main treatment period is not the same outcome as a broader measure over the overall period, a bleeding endpoint, or a thrombotic-burden endpoint. Multiple secondary outcomes can add descriptive context, but unadjusted analyses across many outcomes require restraint.

Finally, planning calculations based on the observed effect are not a substitute for the original design justification and are not observed power. Clear separation of planning assumptions, trial design, sponsor analysis, and recalculation helps readers understand what the registry record establishes and what remains uncertain.

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 registry record does not report the non-inferiority margin, the detailed statistical analysis plan, model covariates, or the sponsor’s narrative conclusion. Those omissions limit independent evaluation of the formal Cox analysis. Although the endpoint is described as adjudicated and the study as blinded endpoint evaluation, the record does not explain the adjudication process or identify who was masked.

The primary endpoint has few observed events, and its confidence interval is broad enough to include differences in either direction. This limits precision. The posted primary endpoint arm counts are based on 145 and 141 participants, while registered enrollment is 290; the registry record does not explain the difference in these figures for this endpoint. The endpoint population is called modified intent-to-treat, but its detailed definition is not reported in the endpoint information.

Missing-data amounts, reasons for missingness, and methods for handling incomplete endpoint follow-up are not reported in the registry record. The record also does not report censoring details for the Cox model, interim-analysis procedures, or the original sample-size justification. These gaps prevent a complete assessment of the analysis assumptions and the study’s planned precision.

The open-label design could affect behavior or outcome reporting, although the trial is described as having blinded endpoint evaluation. The posted description does not provide enough detail to assess how endpoint blinding was implemented. The registry also does not specify the particular standard-of-care medicines in the arm description, and the edoxaban dose is described as age-, weight-, and renal-function-appropriate rather than reported as a complete regimen.

Secondary results cover differing timeframes and outcome definitions, and a multiplicity strategy is not reported. They should therefore be interpreted cautiously, especially when used to support claims beyond the primary endpoint. These limitations do not invalidate the posted results; they define the boundaries of what can be assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Hokusai Study in Pediatric Patients With Confirmed Venous Thromboembolism (VTE) — NCT02798471.
• Registry record last updated 2025-02-28; status last verified 2025-02.
• Results first posted 2023-03-06.
• 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 randomized Phase 3 trial compared edoxaban with standard of care in pediatric participants from birth to less than 18 years of age with confirmed VTE. It is described as open-label with blinded endpoint evaluation and as a parallel-group, multicenter study. Registered enrollment was 290.

The primary outcome was adjudicated symptomatic recurrent VTE from randomization to Month 3, assessed in the modified intent-to-treat population. The registry reports 5 events among 145 participants assigned to edoxaban and 2 among 141 assigned to standard of care. The sponsor-reported Cox analysis gave a hazard ratio of 1.01, a 95% confidence interval from 0.594 to 1.719, and p = 0.969; it is labeled as non-inferiority.

A simple unadjusted recalculation gives a risk difference of 0.020, with a 95% confidence interval from -0.015 to 0.056 and p = 0.267. The estimates are imprecise, and the registry record does not report the non-inferiority margin, missing-data procedures, multiplicity strategy, or original sample-size justification. Secondary outcomes and safety counts provide additional descriptive context but do not resolve those uncertainties.