Non-vitamin K Antagonist Oral Anticoagulants in Patients With Atrial High Rate Episodes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Non-vitamin K Antagonist Oral Anticoagulants in Patients With Atrial High Rate Episodes (NCT02618577), a randomized phase 3 study. The primary outcome is Composite of Stroke, Systemic Embolism, or Cardiovascular Death.

2. Clinical Question

3. Trial Design

NOAH is described in the registry record as an investigator-initiated, prospective, randomized, double-blind, parallel-group, multicentre trial, initiated by the European Society of Cardiology and AFNET. The listed phase is Phase 3. The sponsor is the Atrial Fibrillation Network. The study was designed to compare edoxaban with an ASA-or-placebo strategy in patients with AHRE, and the objective refers to participants with at least two stroke risk factors but without AF.

The registry lists enrollment as 2608. The recorded start is 2016-02, and the primary completion date is 2022-12-31. The study status is terminated. The registry record does not explain the reason for termination, so no cause should be inferred from the status alone. It also does not report the original design assumptions or a sample-size justification. The enrollment figure should therefore be read as the registry’s enrollment entry, not as evidence about why the trial stopped or whether its planned statistical goals were met.

Randomization and double masking are stated characteristics of the design. The parallel-group structure means participants were assigned to a study group rather than receiving both strategies in sequence. The record names edoxaban and ASA as drug interventions, while the comparator arm is called ASA or Placebo. The available arm descriptions do not fully specify the comparator regimen, and the edoxaban dose description is incomplete. A fuller protocol-level account of treatment implementation is not reported in the registry record.

The primary outcome timeframe is 28 months. The primary analysis population is the modified intention-to-treat population, defined in the registry as randomized patients with a qualifying AHRE and intake of at least one dose of study drug. That definition is narrower than all randomized patients because it includes a study-drug exposure condition. The registry does not describe the handling of participants who did not meet that condition or the handling of missing outcome information.

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

Analysis population for the primary outcome, as defined in the registry: The primary analysis is in the modified intention-to-treat population, consisting of all randomised patients with a qualifying AHRE and intake of at least one dose of study drug.

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 Composite of Stroke, Systemic Embolism, or Cardiovascular Death, measured over 28 months.

The primary endpoint is the composite of stroke, systemic embolism, or cardiovascular death. It measures the time from randomization to the first occurrence of one of those events and reports the incidence of first occurrence as a rate per 100 patient-years over a 28-month timeframe. The endpoint is therefore about the first qualifying event for each participant, rather than a count of every repeat event.

A composite endpoint can capture several clinically important event types in one analysis. In general, this can make an outcome more informative when the component events share a clinical rationale, while also making interpretation dependent on which components contribute to the observed result. The registry lists stroke separately among secondary outcomes, but it does not provide component-level primary-outcome event counts in the posted primary result. The relative contribution of stroke, systemic embolism, and cardiovascular death to the composite is therefore not reported in the registry record.

Using a rate per patient-years expresses events in relation to time at risk, rather than presenting only a proportion of participants with an event. This is useful when follow-up time varies. It does not, by itself, show how long each participant was followed or how event risk changed over time. The posted rates are 3.3 for edoxaban and 4.0 for ASA or Placebo, in number of new events per 100 patient-years. The rate comparison should be interpreted together with its confidence interval and with the sponsor’s adjusted time-to-event analysis.

7. Results Posted in the Registry

• Edoxaban: 3.30 versus 4.00 (number of new events per 100 pat.-years) on control; rate ratio 0.83 (95% CI 0.63–1.08, approximate, Poisson model); p ≈ 0.160.

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.

Components of the Primary Outcome, Stroke

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Edoxaban: 0.90 versus 1.10 (number of new events per 100 pat.-years) on control; rate ratio 0.82 (95% CI 0.49–1.37, approximate, Poisson model); p ≈ 0.443.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), 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.

All-cause Death

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Edoxaban: 4.30 versus 3.70 (number of new events per 100 pat.-years) on control; rate ratio 1.16 (95% CI 0.90–1.50, approximate, Poisson model); p ≈ 0.249.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), 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.

Major Bleeding Events

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Edoxaban: 2.10 versus 1.00 (number of new events per 100 pat.-years) on control; rate ratio 2.10 (95% CI 1.35–3.25, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Edoxaban than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results give a mixed picture. The direction of the stroke estimate is lower in the edoxaban group, whereas the directions for all-cause death and major bleeding are higher. The precision differs across these endpoints, and the registry’s adjusted analyses are available for the listed secondary outcomes. These findings add context to the primary composite, but they do not form a uniformly consistent pattern of effects across outcomes.

The primary result remains the central comparison because it was designated as the primary endpoint. Secondary outcomes can help describe which events may contribute to the broader clinical picture, but they cannot independently resolve uncertainty in the primary result. The registry lists 10 secondary outcomes as posted and 12 analyses overall. The outcome list includes components of the primary outcome, major adverse cardiac events, all-cause death, major bleeding, quality of life, patient satisfaction, cost effectiveness and health resource utilisation, and autonomy status. Not all listed outcomes have detailed results in the entries.

Multiple testing matters because examining many outcomes creates more opportunities for apparently notable results to arise by chance. The secondary recalculated p-values are unadjusted, and multiplicity handling is not reported in the registry record. Accordingly, a nominally small p-value for a secondary outcome should not be treated as conclusive evidence by itself. The secondary results are best read as exploratory evidence that can inform further assessment, with attention to their confidence intervals, analysis methods, and relationship to the prespecified primary question.

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

• Components of the Primary Outcome, Stroke
• Major Adverse Cardiac Events (MACEs: Cardiac Death, Myocardial Infarction, Acute Coronary Syndrome (ACS)
• All-cause Death
• Major Bleeding Events
• Quality of Life Changes at 12 and 24 Months Compared to Baseline
• Patient Satisfaction at 12 and 24 Months Compared to Baseline
• Cost Effectiveness and Health Resource Utilisation
• Autonomy Status

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is reported as an event rate per 100 patient-years. This is a rate measure: the numerator concerns new events and the denominator reflects accumulated time at risk. In general, rates are helpful when people contribute different amounts of observation time. A rate is not the same as the percentage of participants who experienced an event, and the posted rate alone does not show the distribution of follow-up time.

What does the recalculated rate ratio describe?

The rate ratio compares the edoxaban rate with the ASA-or-placebo rate. A value of 1 represents equal rates; a value below 1 represents a lower estimated rate in the edoxaban group, and a value above 1 represents a higher estimated rate. For the primary endpoint, the recalculated rate ratio is 0.825. This is a simple, unadjusted recalculation from the posted summary statistics. It is not a substitute for the sponsor’s adjusted cause-specific hazard model.

The posted comparison is marked as Poisson-based. In general, Poisson methods are commonly used for event counts, especially when an exposure-time denominator is available. Such methods rely on assumptions about the event-generating process. Over-dispersion occurs when observed variability is greater than a simple Poisson model would expect; if present and not accounted for, it can make uncertainty estimates too narrow. The registry record does not report a dispersion estimate or a separate adjustment for over-dispersion. That limits assessment of how well this assumption fits the observed data.

How does the sponsor’s model differ?

The sponsor reports an adjusted cause-specific hazard ratio from a cause-specific Cox proportional hazards model for the primary comparison. A hazard ratio compares the instantaneous event rates among people who remain at risk at each point in follow-up, under the model. “Cause-specific” indicates that the model focuses on the event type of interest in the presence of other event types that may prevent that event from occurring later. The reported primary hazard ratio is 0.81. Its 95% confidence interval is 0.6 to 1.08, and its p-value is 0.15.

The registry does not identify the covariates used for adjustment in the reported analysis. It also does not report model diagnostics or the details of how proportional hazards were assessed. The adjusted hazard ratio and the recalculated rate ratio can be compared as complementary summaries, but they should not be treated as identical estimates. The adjusted model uses a time-to-event framework, while the recalculation uses posted group rates without adjustment.

What do the interval and p-value communicate?

A confidence interval describes the range of values reasonably compatible with the data and the analysis assumptions at the stated confidence level. It communicates precision as well as direction. The primary recalculated 95% interval, 0.631 to 1.079, includes 1, the value corresponding to equal rates. The reported p-value of 0.16 is also not a small p-value under commonly used conventions. Neither statistic establishes that there is no difference; both indicate that the observed data do not sharply distinguish the estimated effect from the null.

A p-value is a measure of how incompatible the observed data are with a specified null model, given the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The p-value for the recalculation is unadjusted. The sponsor’s p-value comes from its adjusted model, so the two values reflect different analyses.

What does the analysis population mean?

The registry defines the primary analysis population as modified intention-to-treat: randomized patients with a qualifying AHRE and intake of at least one dose of study drug. This population retains randomization as the starting point but applies the stated qualifying-event and exposure conditions. It is not described as an analysis of every randomized participant regardless of treatment intake. The record does not provide a detailed account of exclusions, missing outcomes, or sensitivity analyses for the primary endpoint.

In general, an analysis population can affect how well a randomized comparison preserves the balance created by randomization. The stated definition should therefore accompany interpretation of the result. The registry does not report enough detail to assess the impact of the population restriction or missing data on the estimate.

Why are secondary results different in status?

Secondary outcomes can provide information about particular event types and other dimensions of health, but repeated testing across outcomes increases the chance that some results will appear noteworthy by chance. A multiplicity procedure can control that risk, but the registry record does not report whether such a procedure was planned or used. The secondary p-values posted for recalculated comparisons are unadjusted. They should be interpreted as supporting context, not as a set of independent confirmatory findings.

11. Confidence Intervals and Precision

Precision is conveyed most directly by the confidence interval around an estimate. For the primary recalculated rate ratio, the 95% interval is 0.631 to 1.079 around an estimate of 0.825. The interval includes 1, the rate-ratio value corresponding to no difference. It allows for a range of possible comparative effects, including a lower rate with edoxaban and values on the other side of the null. The data therefore do not pin down the size or direction of the underlying difference with high precision.

The sponsor’s adjusted primary estimate is a cause-specific hazard ratio of 0.81, with a 95% interval from 0.6 to 1.08. This interval also includes 1. Its breadth reinforces that the adjusted estimate is uncertain. The sponsor’s model and the recalculation use different measures and methods, so their intervals are not interchangeable, even though they point to a similar general level of uncertainty.

Some secondary estimates are less precise than others. The stroke rate ratio is 0.818, with a 95% interval from 0.490 to 1.366. The all-cause death rate ratio is 1.162, with an interval from 0.9 to 1.501. The major bleeding rate ratio is 2.1, with an interval from 1.355 to 3.255. The intervals and p-values should be read alongside the nature of each outcome and the multiplicity concern, not as a ranked set of definitive claims.

In general, a confidence interval’s width depends on the amount and variability of information available and on the analysis model. The registry does not report dispersion measures for these event rates, and it does not provide detailed missing-data procedures or model diagnostics. Those omissions constrain a fuller assessment of precision. A confidence interval also reflects statistical uncertainty under its assumptions; it does not capture every source of uncertainty, such as incomplete reporting or uncertainty about the analysis choices.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not a record of the trial’s original design calculation. For these rate-based outcomes, the figures are participants per arm. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario asks what participant count would be needed to detect the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents a planning target under which a study would have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher chance of detection under the same general framework and therefore calls for a larger planned sample. These figures are planning quantities, not a retrospective measure of the trial’s performance.

For the primary comparison, planning for 100% of the observed effect gives 5,027 participants per arm for 80% power and 6,730 participants per arm for 90% power. Planning for 75% of the observed effect gives 8,707 participants per arm for 80% power and 11,656 participants per arm for 90% power. Planning for 50% of the observed effect gives 19,098 participants per arm for 80% power and 25,566 participants per arm for 90% power. The smaller the effect a future study aims to detect, the more participants it generally needs, all else being equal.

These calculations are not observed power. They are prospective planning illustrations that depend on the stated assumptions and the observed effect used as their starting point. They do not establish whether the trial was adequately designed or explain its termination. The registry record does not report the trial’s own original sample-size assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.0400; treatment rate λ₁ = 0.0330 events per patient-year; follow-up T = 2.33 years.
2. n = (1.96 + 0.842)² × (1/0.0400 + 1/0.0330) / (2.33 × [ln(0.825)]²) = 5,026.9, rounded up to 5,027 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
lambda0 <- 0.04                      # control rate, events per patient-year
lambda1 <- 0.033                      # treatment rate
tt      <- 2.33333333333333                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2618577)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 5,027 (80% power), 6,730 (90% power)
 75% of observed effect: n per arm = 8,707 (80% power), 11,656 (90% power)
 50% of observed effect: n per arm = 19,098 (80% power), 25,566 (90% power)
Simulated power, Poisson counts, n = 5,027 per arm: 0.804
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.630

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is an adjusted cause-specific Cox proportional hazards model. It reports a hazard ratio of 0.81, a 95% confidence interval from 0.6 to 1.08, and p = 0.15. The simple recalculation from the posted summary rates gives an unadjusted rate ratio of 0.825, a 95% confidence interval from 0.631 to 1.079, and an unadjusted p-value of 0.16.

The two estimates are similar in broad direction and both have intervals that include the null value of 1. That similarity is reassuring as a description of the broad pattern, but it does not make the analyses equivalent. The sponsor’s estimate is adjusted and is based on a cause-specific time-to-event model. The recalculated estimate compares posted rates without adjustment. The registry does not identify the adjustment covariates, so the adjusted result cannot be independently reconstructed from the reported information.

The recalculation is a transparent summary derived from the posted rates, not a replacement for the sponsor’s model. The sponsor’s own analysis is the primary reported analysis and should guide interpretation of the registry’s adjusted result. The posted estimates do not establish a clear difference in the primary endpoint, and neither analysis demonstrates that the groups have identical outcomes.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes. This distinction helps organize interpretation: the primary endpoint addresses the main comparison, while secondary outcomes provide additional information. However, the registry record does not report whether a multiplicity strategy was specified or applied. It does not say whether testing across secondary outcomes was adjusted, whether a hierarchy was used, or whether particular secondary findings were designated confirmatory.

Without a reported multiplicity procedure, secondary p-values should be treated as unadjusted evidence. When many outcomes are examined, the probability of observing at least one small p-value by chance can increase. That general concern does not mean a secondary result is false; it means that isolated nominal results carry less evidential weight unless supported by a prespecified testing strategy or other corroborating evidence. The posted secondary findings should therefore be interpreted in relation to the primary result and the uncertainty in each estimate.

The primary analysis population is described as modified intention-to-treat and includes randomized patients with a qualifying AHRE who took at least one dose of study drug. The record does not report a full accounting of exclusions from this population or a comparison of included and excluded participants. It also does not describe how missing outcome data were handled, whether censoring rules were prespecified, or whether sensitivity analyses assessed the impact of missingness.

These are important reporting limits. In general, missing-data choices and analysis-population definitions can affect an estimate, especially when missingness is related to prognosis or treatment. The registry record does not provide enough information to determine whether such concerns materially affected these results. Interim analyses, stopping rules, and the broader statistical analysis plan are also not reported in the registry record. The terminated status alone does not establish whether or how any of these procedures influenced the study.

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: death (7.9%), viral test negative (7.3%), cardiac failure (7.1%), pneumonia (4.4%), transfusion (4.4%).

The registry lists serious adverse events for 1306 participants at risk in the edoxaban group, with 498 affected, and for 1302 participants at risk in the ASA-or-placebo group, with 467 affected. Other adverse events are listed for the same at-risk counts, with 718 affected in the edoxaban group and 662 in the comparator group. Deaths are listed as 142 and 125, respectively. These are registry counts; they are not rates adjusted for exposure time.

The serious-event terms most commonly listed include Death at 7.9%, Viral test negative at 7.3%, Cardiac failure at 7.1%, Pneumonia at 4.4%, Transfusion at 4.4%, and Cardiac pacemaker replacement at 4.4%. These percentages are reported as registry entries. The record does not provide the denominator or further detail for each term in the listed material, so they should not be converted into counts or compared as if their definitions and observation periods were fully specified.

Serious adverse events are not necessarily events caused by treatment. The registry entries do not establish causality, severity beyond the serious-event classification, or the timing of each event. A fuller safety interpretation would require those details and the protocol’s definitions and attribution procedures, which are not reported in the registry record.

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

The primary result is an estimate of the relative event rate for stroke, systemic embolism, or cardiovascular death in the edoxaban group compared with the ASA-or-placebo group. The observed rates are 3.3 and 4.0 new events per 100 patient-years, respectively. The recalculated rate ratio is 0.825, and the sponsor’s adjusted hazard ratio is 0.81. Both estimates point toward a lower rate or hazard in the edoxaban group, but both confidence intervals include 1. The posted data therefore do not provide a precise, definitive estimate of the comparative effect.

This result does not demonstrate that the treatments have identical effects. A confidence interval that includes the null can still include effects that could matter, in either direction. Nor does the result establish that edoxaban is superior on the primary outcome: the sponsor’s adjusted p-value is 0.15, and the unadjusted recalculated p-value is 0.16. The correct interpretation is uncertainty about the size and direction of the primary comparison, not proof of no effect or proof of benefit.

The secondary results give additional but limited context. Their directions are mixed, and multiple testing handling is not reported. The major bleeding result is one part of that wider pattern, but the registry entries do not establish that the events were caused by treatment. Safety counts should be considered alongside the primary and secondary efficacy estimates, while recognizing the limits of the available detail.

These findings apply to the population and analysis definition recorded for this trial. The registry objective describes patients with AHRE, stroke risk factors, and no AF; the primary analysis population requires qualifying AHRE and intake of at least one dose of study drug. The record does not support extending the result to populations or treatment circumstances not described. The terminated study status also does not, by itself, explain the reason for termination or change the statistical meaning of the posted estimates.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to interpret an uncertain primary estimate alongside multiple secondary outcomes and safety counts. The primary rate ratio is below 1, but its confidence interval includes 1. The sponsor’s adjusted cause-specific hazard ratio has a similar direction and likewise includes the null. Reading the point estimate alone would give an incomplete account; precision and analysis method are essential parts of the interpretation.

The record also illustrates why an event rate and a hazard ratio should not be treated as interchangeable. The rate-based recalculation is an unadjusted comparison of posted summary rates. The sponsor’s Cox model estimates an adjusted cause-specific hazard ratio using a time-to-event framework. Their broad similarity does not remove the differences in estimand, adjustment, and assumptions.

Secondary results can help clarify the pattern across specific outcomes, but the presence of several outcomes makes multiplicity relevant. With no multiplicity procedure reported, secondary p-values should not be read as a collection of independent confirmations. The mixed directions across the posted secondary endpoints make it particularly important to avoid relying on any single secondary estimate without considering its interval and context.

Finally, planning illustrations based on the observed effect are not the same as the trial’s original design rationale or an evaluation of observed power. The registry does not report the original sample-size assumptions, multiplicity plan, interim procedures, or detailed missing-data methods. Distinguishing what the record reports from what remains unreported is central to a careful statistical reading.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record leaves several trial-specific questions unanswered. It lists a terminated status but does not give a reason for termination. It does not report whether a stopping rule or interim analysis was used, or whether either influenced the study’s conduct. The original sample-size justification and design assumptions are also not reported, so the planning illustrations based on observed effects cannot be used to reconstruct the original rationale.

The primary analysis population is defined as randomized patients with a qualifying AHRE and at least one dose of study drug, but the record does not provide a detailed flow of participants into that population. It does not report how missing outcomes were handled, how follow-up ended, or whether sensitivity analyses were conducted. These omissions limit assessment of possible effects of exclusions, censoring, and missing data.

The sponsor’s primary model is identified as an adjusted cause-specific Cox proportional hazards model, but its adjustment variables and diagnostic checks are not reported. The registry also does not state whether multiplicity adjustments were made for secondary outcomes. These details would help assess model assumptions and the evidential status of secondary findings.

Some treatment descriptions are incomplete. The edoxaban dose description ends before all reduction criteria are fully stated, and the ASA-or-placebo description does not provide a complete account of the comparator strategy. The registry’s safety entries also lack detail on event timing and causal attribution. These limitations should temper interpretation without implying that the unreported procedures or information had any particular result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Non-vitamin K Antagonist Oral Anticoagulants in Patients With Atrial High Rate Episodes — NCT02618577.
• Registry record last updated 2025-02-06; status last verified 2025-02.
• Results first posted 2025-02-06.
• 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

The registry record describes NOAH as a Phase 3 randomized, double-blind, parallel-group trial sponsored by the Atrial Fibrillation Network. It lists enrollment as 2608, a start of 2016-02, primary completion on 2022-12-31, and status as terminated. The comparison is edoxaban versus ASA or Placebo.

The primary endpoint is first stroke, systemic embolism, or cardiovascular death, expressed as new events per 100 patient-years over 28 months. The primary recalculated rate ratio is 0.825, with a 95% confidence interval from 0.631 to 1.079 and unadjusted p = 0.16. The sponsor reports an adjusted cause-specific hazard ratio of 0.81, with a 95% confidence interval from 0.6 to 1.08 and p = 0.15. Both estimates leave substantial uncertainty about the comparative effect.

The posted secondary findings have mixed directions, and serious adverse event and other safety counts are recorded by group. Multiplicity procedures, detailed missing-data methods, the original sample-size justification, and the reason for termination are not reported in the registry record.