EINSTEIN Junior: Oral Rivaroxaban in Children With Venous Thrombosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for EINSTEIN Junior: Oral Rivaroxaban in Children With Venous Thrombosis (NCT02234843), a randomized phase 3 study. The primary outcome is Incidence Rates of All Symptomatic Recurrent Venous Thromboembolism During the Main Treatment Period.

2. Clinical Question

The primary outcome captures a clinically important recurrence during treatment, but it is a binary event outcome rather than a continuous measure of clot burden or drug exposure. The registry reports group percentages with confidence intervals and also reports an exploratory Cox model. Those summaries address related but different statistical questions: the percentages describe the proportion with an event, while a hazard ratio compares event rates over time under the model. Neither estimate alone describes every aspect of efficacy or safety.

3. Trial Design

This was a randomized, parallel-group, active-controlled phase 3 study. The official title describes it as multicenter and open-label; the registry records no masking. The trial compared age- and body-weight-adjusted rivaroxaban with standard care for children with acute venous thromboembolism. Enrollment is listed as 500, and the record lists the study as completed.

The rivaroxaban regimen included tablets and oral suspension. Dosing varied according to age and body weight, with the stated aim of achieving exposure similar to that seen in adults treated for venous thromboembolism with 20 mg rivaroxaban. Standard care could consist of low molecular weight heparin, fondaparinux, and/or a vitamin K antagonist, given according to standard care. The record does not describe a single fixed comparator regimen.

The primary endpoint covered the main study treatment period. This was 3 months, except for children with central venous catheter venous thromboembolism aged <2 years, for whom the period was 1 month. The endpoint population is identified as the full analysis set. The registry also lists pharmacokinetic measures, prothrombin-time measures, and other clinical outcomes among secondary outcomes.

The trial's original sample-size justification, design assumptions, interim-analysis plan, and detailed statistical-analysis plan are not reported in the registry record. The planning illustrations discussed separately are recalculations based on the observed effect and are not evidence of the trial's original design rationale.

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 520 children were screened for this study. Twenty children did not pass the screen of inclusion/exclusion criteria. A total of 500 children were randomized 2:1 to study treatment.

Only the first 6 of 10 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS)

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.

Only the first 6 of 11 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Incidence Rates of All Symptomatic Recurrent Venous Thromboembolism During the Main Treatment Period, measured over During the main study treatment period (i.e., 3 months, except for children with central venous catheter venous thromboembolism (CVC-VTE) aged <2 years for whom it was 1 month).

The primary endpoint is the incidence of all symptomatic recurrent venous thromboembolism during the main treatment period. The record states that a central independent adjudication committee classified symptomatic recurrent events. Incidence is defined as the number of participants having the event in the time window divided by the number of participants in the reference population. The reported unit is percentage of participants, and the endpoint population is the full analysis set.

This endpoint is used to assess recurrence during the treatment period, rather than drug concentration, clot burden alone, or a laboratory measure. A percentage gives an absolute description of how often the event occurred in each group. The associated confidence interval conveys uncertainty around each group estimate, which is important when events are uncommon and estimates can be imprecise.

The main treatment period was 3 months, with a 1-month period for children with central venous catheter venous thromboembolism aged <2 years. Because the observation period is not identical for that subgroup, the reported endpoint should be understood in the context of the registry's stated timeframe. The record's separate composite secondary endpoint adds asymptomatic deterioration in thrombotic burden on repeat imaging; that is not part of the primary endpoint.

7. Results Posted in the Registry

• Rivaroxaban Group: 1.2% (4/335) versus 3.0% (5/165) on control; risk difference -1.8 percentage points (95% CI -4.7 to 1.0), risk ratio 0.39 (0.11–1.45); unadjusted two-proportion z-test p = 0.146.

8. Secondary Efficacy Endpoints

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

Incidence Rates of the Composite of All Symptomatic Recurrent Venous Thromboembolism and Asymptomatic Deterioration in Thrombotic Burden on Repeat Imaging During the Main Treatment Period

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Rivaroxaban, Aged 12-<18: 2.2% (4/184) versus 4.3% (4/92) on control; risk difference -2.2 percentage points (95% CI -6.8 to 2.5), risk ratio 0.50 (0.13–1.95); unadjusted two-proportion z-test p = 0.310.
  • Rivaroxaban, Aged 6-<12: 0.0% (0/67) versus 4.3% (4/92) on control; risk difference -4.3 percentage points (95% CI -8.5 to -0.2); unadjusted two-proportion z-test p = 0.084.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rivaroxaban, Aged 12-<18 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 Rivaroxaban, Aged 6-<12 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several types of questions. One is a composite of symptomatic recurrent venous thromboembolism and asymptomatic deterioration in thrombotic burden on repeat imaging. Other listed outcomes concern plasma exposure and peak or trough concentrations, as well as prothrombin-time ratios in age groups and dosing schedules. These measures complement the primary clinical endpoint by describing imaging findings, pharmacokinetics, or laboratory response; they do not measure the same outcome as symptomatic recurrence.

The posted age-stratified composite results vary across age groups and have wide confidence intervals in several small groups. Some displayed groups have no observed events, but their intervals still extend above zero. That pattern illustrates why a zero point estimate in a small subgroup does not establish that the underlying event risk is zero. The subgroup estimates are less precise and should not be treated as definitive comparisons.

The primary result concerns symptomatic recurrence in the full analysis set. Secondary composite and age-specific summaries can add context, but they cannot overturn or replace the primary endpoint result. In particular, age-stratified estimates involve smaller groups and may be more sensitive to a small number of events. The registry lists 28 secondary outcomes as posted, while the record also notes 35 outcome measures overall.

Unadjusted secondary results carry less weight when many outcomes and subgroup comparisons are examined. In general, looking across numerous outcomes increases the chance that some results will appear unusual by chance. The registry record does not report a multiplicity adjustment or a hierarchy for secondary analyses. Secondary findings should therefore be viewed as supportive or exploratory unless their inferential status is otherwise established in the registry record. The result summaries do not justify treating any isolated secondary comparison as conclusive evidence.

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

• Incidence Rates of the Composite of All Symptomatic Recurrent Venous Thromboembolism and Asymptomatic Deterioration in Thrombotic Burden on Repeat Imaging During the Main Treatment Period
• AUC(0-24)ss in Plasma
• Cmax,ss in Plasma
• Ctrough,ss in Plasma
• Prothrombin Time (PT) Ratios to Baseline: Rivaroxaban Administered Once Daily (Suspension and Tablet) in the Age Group 12-<18 Years
• Prothrombin Time (PT) Ratios to Baseline: Rivaroxaban Administered Once Daily (Suspension and Tablet) in the Age Group 6-<12 Years
• Prothrombin Time (PT) Ratios to Baseline: Rivaroxaban Administered Twice Daily (Suspension and Tablet) in the Age Group 6-<12 Years
• Prothrombin Time (PT) Ratios to Baseline: Rivaroxaban Administered Twice Daily (Suspension) in the Age Group 2-<6 Years

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a binary outcome: each participant either had a symptomatic recurrence during the relevant period or did not. The registry expresses that outcome as a percentage of participants and supplies a confidence interval for each group. The comparison also includes an unadjusted recalculation of the risk difference and an unadjusted p-value. Separately, the registry reports the sponsor's exploratory Cox proportional hazards analysis.

What does a percentage estimate?

A group percentage estimates the proportion of the reference population that experienced the event within the stated timeframe. It is an absolute measure, so it can be read without first choosing a comparator group. The registry defines the numerator as the number of participants with an event in the time window and the denominator as the number of participants in the reference population. That makes it important to pay attention to the analysis population and the stated treatment period when interpreting the estimate.

The percentage is not a count of all clinical events if a participant can have recurrent events; the record's endpoint definition describes the number of participants having the event. Nor is it an annualized rate. The registry calls the measure an incidence rate but reports it as a percentage of participants, with the stated risk-population definition.

What does a risk difference add?

A risk difference expresses the absolute separation between the group proportions. A value of zero corresponds to no difference in the estimated proportions. The unadjusted recalculation uses the posted group summaries rather than an adjusted model. Its confidence interval includes zero, and its unadjusted p-value is 0.146. This is evidence of uncertainty in the comparison, not a demonstration that the groups are identical.

A risk difference is distinct from a relative measure. A relative measure scales one group's outcome against the other group's outcome, while a risk difference stays on the percentage-point scale. With sparse outcomes, relative estimates can be particularly sensitive to small changes in counts. The posted analysis also includes risk-ratio and odds-ratio recalculations, but the main interpretive emphasis remains on the reported group percentages and the sponsor's own analysis.

Why use a Cox model?

In general, a Cox proportional hazards model analyzes time to an event and compares hazards between groups. It can use information about when events occur, rather than only whether an event occurred by the end of a period. Its hazard ratio is a relative, model-based summary and depends on the model's assumptions. In general, the proportional-hazards assumption means that the relative hazard is treated as stable over time. The registry labels its Cox analysis exploratory and reports a hazard ratio of 0.4 with a 95% confidence interval from 0.11 to 1.41.

A hazard ratio is not a risk difference, and it should not be translated directly into an absolute percentage change. The Cox estimate and the unadjusted percentage comparison can differ because they summarize the data differently. The registry record does not report further details about model covariates or diagnostics, so those aspects cannot be assessed from the record.

Why do sparse events matter?

When event counts are low, each event represents a larger share of the observed information. This can make the estimated group comparison unstable and widen uncertainty. The primary outcome counts are small, and the confidence intervals for the group percentages extend across a substantial range. In general, sparse data can also make standard approximations less reliable, especially for relative estimates. These considerations favor emphasizing the confidence intervals and study context rather than relying on a single point estimate or p-value.

Over-dispersion is a general issue in some count-data settings: observed variation exceeds what a simple model expects, making standard errors too small if the extra variation is ignored. The primary endpoint is reported as a binary participant outcome, not as a count rate with a stated over-dispersion model. The registry record does not report an over-dispersion adjustment, so such an adjustment should not be assumed.

What does the p-value tell the reader?

In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the chosen analysis assumptions. It does not give the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The unadjusted p-value of 0.146 should therefore be read alongside the estimated group percentages and their confidence intervals, not as a stand-alone conclusion.

The record's reported Cox analysis is identified as exploratory. The registry does not report whether the primary endpoint had a prespecified inferential hierarchy or how analyses across multiple outcomes were handled. Those omissions limit interpretation of formal claims across the full set of endpoints.

11. Confidence Intervals and Precision

The primary group estimates are 1.2% for rivaroxaban, with a 95% confidence interval from 0.4% to 3.0%, and 3.0% for the comparator, with a 95% confidence interval from 1.2% to 6.6%. A confidence interval describes the statistical uncertainty around an estimated quantity under the analysis method. It does not mean that a fixed proportion of individual outcomes must lie inside the interval.

The intervals are broad relative to the point estimates, which reflects limited precision in the event-rate estimates. They overlap, and the recalculated risk-difference interval includes no difference. Taken together, the estimates are compatible with a range of comparative outcomes. The data do not pin down the size of a difference precisely, even though the observed percentages are not the same.

The exploratory Cox result has a hazard ratio of 0.4 and a 95% confidence interval from 0.11 to 1.41. Since that interval includes 1, it also leaves substantial uncertainty about the relative hazard. The hazard-ratio interval and the intervals for the group percentages concern different statistical quantities, so their widths and values should not be compared as if they were measuring the same thing.

In general, confidence intervals tend to be less precise when events are uncommon or the amount of information is limited. The primary event counts are 5 and 4, so the small number of observed events is central to reading the uncertainty. Confidence intervals describe statistical precision under an analysis; they do not account for every potential limitation, such as missing outcome data or model misspecification. The registry record does not report enough detail to assess all such sources of uncertainty.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations translate the observed effect into hypothetical sample-size requirements. These are participants per arm, not total participants or total events. For a time-to-event outcome, the planning convention would instead be total events, but the primary endpoint is a binary participant outcome and the stated figures are participants per arm.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at 100%, 75%, or 50% of the observed effect. The registry's original design assumptions and sample-size justification are not reported, so these calculations should not be mistaken for the trial's planned enrollment target.

The 80% power column gives the illustrative number of participants per arm needed for an 80% chance of detecting the stated effect under those assumptions, if that effect were the true effect. The 90% power column gives the corresponding requirement for a 90% chance. For the primary outcome, the illustrations are 962 participants per arm for 100% of the observed effect, 1,892 for 75%, and 4,664 for 50% at 80% power. At 90% power, the corresponding figures are 1,287, 2,532, and 6,244.

Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. These are planning illustrations based on the observed effect, not observed power. They should be interpreted as demonstrations of how assumptions affect planning, not as a retrospective judgment of whether the completed trial was adequate.

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 = 0.030; treatment proportion p₁ = 0.012; average p̄ = 0.021.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2033 = 0.3986.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2029 = 0.1708.
4. n = (0.3986 + 0.1708)² / (-0.0184)² = 961.4, rounded up to 962 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 <- 0.0303030303030303                          # control proportion
p1 <- 0.0119402985074627                          # 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(2234843)
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 = 962 (80% power), 1,287 (90% power)
 75% of observed effect: n per arm = 1,892 (80% power), 2,532 (90% power)
 50% of observed effect: n per arm = 4,664 (80% power), 6,244 (90% power)
power.prop.test: 961.4 
Simulated power at n = 962 per arm: 0.820 (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 reports the sponsor's analysis as an exploratory Cox proportional hazards model. It gives a hazard ratio of 0.4, with a 95% confidence interval from 0.11 to 1.41. The interval includes the hazard-ratio null value of 1, so the estimate is compatible with a range that includes no relative hazard difference.

The unadjusted recalculation uses the posted group percentages to compare absolute risks and reports p = 0.146. It is not a replication of the Cox model: the risk-difference calculation compares event proportions, whereas the Cox model summarizes relative hazards over time. Differences between these approaches need not indicate an error because they target different statistical summaries and can use timing information differently.

The registry does not flag a discrepancy between the posted result and the recalculation. The sponsor's analysis should therefore be read as the reported exploratory time-to-event analysis, alongside the unadjusted absolute comparison, rather than as a replacement for it. The record does not provide the model details needed to evaluate covariate adjustment, diagnostics, or other assumptions beyond identifying the analysis as an exploratory Cox proportional hazards model.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates many outcomes, subgroup comparisons, or analysis choices. In general, the more statistical tests considered, the greater the chance that at least one result will appear notable by chance even when there is no true effect. This matters for EINSTEIN Junior because the registry lists a broad set of secondary outcomes, including a clinical and imaging composite, pharmacokinetic measures, and prothrombin-time measures, and reports 28 secondary outcomes as posted.

The registry record does not report a multiplicity-control strategy, a formal hierarchy among outcomes, or which secondary analyses were intended to be confirmatory. As a result, secondary p-values or subgroup patterns should not be interpreted as if each were an isolated, prespecified test with no other analyses. The primary endpoint remains the clearest focus for interpretation, while secondary analyses provide additional descriptive or exploratory context.

The primary endpoint population is the full analysis set. The registry does not explain how participants with missing primary-outcome information were handled, whether any imputation was used, or what sensitivity analyses assessed missingness. The missing-data assumptions and their possible influence are therefore not reported in the registry record. No conclusion about the impact of missing data should be inferred from the endpoint estimates alone.

The registry also does not report the original sample-size justification, planned interim analyses, or a detailed statistical-analysis plan. The planning illustrations use the observed effect and specified assumptions; they do not establish what the original design anticipated. The available record identifies an exploratory Cox analysis, but does not report enough detail to assess all model specifications or analysis populations for every secondary endpoint.

These omissions do not invalidate the posted results, but they limit what can be established from the registry record. They are reasons to distinguish the reported estimates from stronger claims about prespecification, multiplicity control, missing-data robustness, or the trial's original statistical intent.

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 0% 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 (2.4%), headache (1.9%), vomiting (1.8%), pyrexia (1.8%), seizure (1.2%).

The serious adverse-event summaries report 35 affected participants among 162 at risk in the comparator group and 78 among 329 at risk in the rivaroxaban group. These are counts from the safety summaries, not the primary efficacy population counts. The registry also reports no deaths in the comparator group and 2 in the rivaroxaban group.

The listed serious adverse-event terms include febrile neutropenia at 2.4%, headache at 1.9%, vomiting at 1.8%, pyrexia at 1.8%, seizure at 1.2%, and abdominal pain at 0.9%. These terms and percentages describe reported events; they do not establish that the study treatment caused them. The registry record does not supply a causal attribution for each listed event.

Safety counts should be read with their stated group populations and in the context of the trial's duration and event definitions. Differences in raw counts are not, by themselves, comparative risk estimates, and the counts do not account for possible differences in time at risk. These summaries should not be used alone to draw a broad conclusion about comparative safety.

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

The posted primary results show lower observed symptomatic-recurrence percentages in the rivaroxaban group than in the comparator group: 1.2% versus 3.0%. The confidence intervals are broad, and the unadjusted comparison remains uncertain. The exploratory Cox model also has a confidence interval that includes the no-difference value. The central statistical message is therefore a difference in point estimates accompanied by limited precision, not a definitive estimate of the treatment effect.

The results do not establish that the treatments are equivalent. A failure to demonstrate a clear difference is not the same as evidence that the outcomes are the same. Nor should the observed point estimates be interpreted as proof that one regimen is superior. Few primary events occurred, and the comparison is compatible with a range of underlying effects.

The registry record describes a randomized open-label study, but the statistical summaries do not resolve every question about outcome ascertainment, missing data, or analysis choices. The primary endpoint was classified by a central independent adjudication committee, which is relevant context, but the record does not report all operational details needed to assess every potential source of bias.

The trial's results concern children with acute venous thromboembolism under the study's treatment regimens and follow-up periods. The record's age-stratified secondary results and varied standard-care options indicate that the setting includes clinically different groups and regimens. The primary finding should not be generalized beyond the studied population or interpreted as an individualized treatment recommendation.

Safety findings are also descriptive. Serious adverse-event counts and listed terms provide information about events observed during the study, but do not show whether any event was caused by treatment. Statistical interpretation can describe uncertainty and the structure of evidence; it cannot substitute for clinical judgment or support medical advice.

18. Why This Trial Matters Statistically

This trial presents several statistical challenges common in pediatric studies. The population spans a wide age range, and the rivaroxaban regimen was adjusted for age and body weight. The main comparator was standard care, which could involve different anticoagulant options rather than a single uniform treatment. These features make the study question clinically broad while also requiring careful attention to the definition of each group and outcome.

The primary outcome is uncommon in the posted data. With few events, a small change in the number of outcomes can alter the estimated percentage or comparative effect. Confidence intervals are therefore essential: a point estimate alone conceals how uncertain the comparison is. Here, the arm-specific intervals and the exploratory hazard-ratio interval make clear that the observed estimates do not precisely determine the comparative effect.

The record also illustrates why estimands matter. A percentage with an absolute risk comparison and a Cox hazard ratio are related summaries, but they are not interchangeable. They answer different questions and rely on different analysis structures. Reporting both can be informative if readers understand what each measure means and avoid translating one directly into the other.

Finally, the secondary outcomes cover clinical recurrence, imaging deterioration, drug exposure, and laboratory response. This range can help describe different dimensions of treatment, but it also raises multiplicity and interpretation issues. The primary endpoint offers a clear anchor, while secondary results require attention to precision, subgroup size, and the absence of a reported multiplicity strategy. These are useful lessons for reading randomized trials with sparse events and numerous outcomes.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific limitations unresolved. The study was open-label and had no masking, according to the registry. The primary outcome was classified by a central independent adjudication committee, but the record does not describe further protections against bias in other aspects of trial conduct or outcome collection.

The primary event counts are low, and the confidence intervals are broad. This limits precision for the between-group comparison and makes subgroup estimates especially uncertain. The secondary composite results are separated by age, with small groups and wide intervals in some strata. Those estimates should not be read as stable evidence of differences across age categories.

The treatment period varied for children with central venous catheter venous thromboembolism aged <2 years. The stated period was 1 month for that subgroup and 3 months for others. This difference is important context when interpreting the overall endpoint and comparing participants with different follow-up windows.

Standard care could include low molecular weight heparin, fondaparinux, and/or a vitamin K antagonist. The registry record does not provide enough detail to evaluate how frequently each comparator option was used or whether outcome patterns differed by comparator regimen. Likewise, it does not report the original sample-size justification, missing-data methods, multiplicity strategy, or detailed model diagnostics.

The sponsor's Cox analysis is labelled exploratory, and the record does not give further information about its covariates or assumptions. The registry summaries support cautious description of observed outcomes, but not a full assessment of every design and analysis choice.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: EINSTEIN Junior: Oral Rivaroxaban in Children With Venous Thrombosis — NCT02234843.
• Registry record last updated 2020-04-01; status last verified 2020-03.
• Results first posted 2020-04-01.
• 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

EINSTEIN Junior was a completed randomized, parallel-group, open-label phase 3 study comparing age- and body-weight-adjusted rivaroxaban with standard care in children with acute venous thromboembolism. Enrollment is listed as 500. The primary endpoint was symptomatic recurrent venous thromboembolism during the main treatment period, in the full analysis set.

The registry reports primary event percentages of 1.2% for rivaroxaban and 3.0% for the comparator, with broad confidence intervals. The unadjusted recalculation and exploratory Cox analysis both leave uncertainty about the comparative effect. Secondary outcomes address a clinical and imaging composite, drug exposure, and prothrombin-time measures. Serious adverse events and deaths are also reported descriptively.

The record does not report the original sample-size justification, multiplicity strategy, missing-data methods, or full details of the statistical plan. These gaps, together with the small number of primary events, limit how precisely the comparative results can be interpreted.