Prolongation of the Interval Between Monitoring of Warfarin in Stable Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prolongation of the Interval Between Monitoring of Warfarin in Stable Patients (NCT00356759), a randomized phase 2 study. The primary outcome is Primary Outcome Measure: Time in Therapeutic Range.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 2 trial with triple masking. The registry lists an enrollment of 250 and a completed status. The start is recorded as 2006-12, and primary completion as 2010-01. The sponsor was Hamilton Health Sciences Corporation. Further details about the randomization sequence, allocation concealment, and which trial roles were masked are not reported in the registry record.

The two assigned approaches were dose assessment every 4 weeks and dose assessment every 12 weeks. The 12-weekly arm used sham INRs 2 out of 3 times, while the standard-management arm used true INR values at every assessment. These descriptions define the treatment contrast as a monitoring strategy, rather than a comparison of different anticoagulant drugs. The registry does not report further operational details about how monitoring visits or sham results were administered.

The primary outcome was assessed over 12 months. The primary population is identified as intention to treat. The posted primary results include 126 participants in the 4-weekly arm and 124 in the 12-weekly arm. The registry lists secondary outcomes concerning thromboembolic events, major bleeding, extreme INR results, and dose changes, although the posted secondary results cover only some of those listed outcomes.

The registry record does not report the original sample-size justification, the trial’s planned significance level, or a full statistical analysis plan. Nor does it describe interim analyses or stopping rules. Those design details should not be inferred from the posted results or from the separate planning illustrations based on observed effects.

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: Intention to treat population

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: All patients randomized

6. Primary Endpoint

The registry lists the primary outcome as Primary Outcome Measure: Time in Therapeutic Range, measured over 12 months.

The primary outcome was time in therapeutic range over 12 months, expressed as a percentage of time. The registry says it was calculated by linear interpolation and analyzed as a mean in the intention-to-treat population. The posted results report a mean and standard deviation for each monitoring arm.

In general, time in therapeutic range describes how much of the observed period a patient’s anticoagulation test result is within the target range. The registry summary explains why monitoring is relevant: results outside the treatment range can prompt dose changes, and results that are too low or too high are associated in the summary with different clinical risks. The endpoint therefore provides a measure of how consistently test results remain in the desired range during follow-up.

Using a continuous summary retains information about the amount of time in range rather than reducing each participant to a simple in-range or out-of-range category. A group mean describes the average result, while the standard deviation describes variation among participants. Neither alone shows how individual values were distributed or how many participants had particular clinical events. The registry does not report the target INR range, participant-level trajectories, or additional details about the interpolation procedure.

7. Results Posted in the Registry

• Dose Assessment 12-weekly: mean 71.60 versus 74.10 on control; difference -2.50 (95% CI -7.31 to 2.31), standardized effect d = -0.13; z-test p = 0.309.

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.

Secondary Efficacy Outcomes: Thromboembolic Events

• 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:
  • Dose Assessment 12-weekly: 0.0% (0/124) versus 0.8% (1/126) on control; risk difference -0.8 percentage points (95% CI -2.3 to 0.8); unadjusted two-proportion z-test p = 0.320.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Assessment 12-weekly and the control. The interval gives the range of effects that remain compatible with the data.

Patients With Dose Changes

• 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:
  • Dose Assessment 12-weekly: 37.1% (46/124) versus 55.6% (70/126) on control; risk difference -18.5 percentage points (95% CI -30.6 to -6.3), risk ratio 0.67 (0.51–0.88); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Dose Assessment 12-weekly than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide a limited and uneven set of additional observations alongside the primary time-in-range comparison. One posted comparison concerns thromboembolic events, and another concerns participants with dose changes. Although the registry lists other safety and efficacy outcomes, results for all of those listed measures are not posted. The overall secondary picture is therefore incomplete rather than a comprehensive accounting of every outcome named in the record.

These outcomes address different questions from the primary endpoint. Time in therapeutic range summarizes anticoagulation test results over follow-up, whereas event outcomes count participants experiencing a defined event and dose-change outcomes describe a management consequence. Agreement or disagreement across these measures would not automatically confirm or overturn the primary result: their definitions, frequencies, and statistical precision differ. The secondary results should be viewed as complementary context, not as a replacement for the primary comparison.

In general, testing several outcomes increases the chance that at least one result will appear unusual by chance, even when each test is considered separately. The posted secondary p-values are unadjusted, and the registry does not report a multiplicity procedure or a hierarchy of confirmatory outcomes. Consequently, an isolated secondary association carries less weight than a prespecified primary result with a defined analysis plan. The record also does not report whether the secondary analyses were prespecified in detail, whether any were exploratory, or how missing outcome data were handled.

Secondary findings can still help identify questions for further evaluation, but the registry entries do not establish a broader pattern of treatment benefit or harm. Their interpretation depends on the number of outcomes examined, the completeness of reporting, and uncertainty in each estimate. The available record supports cautious description of the posted comparisons, not a claim that every listed secondary outcome was measured, analyzed, or demonstrated a difference.

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

• Secondary Efficacy Outcomes: Thromboembolic Events
• Secondary Safety Outcome: Major Bleeding
• Secondary Safety Outcome: Number of Patients With Extreme INR Results
• Number of Extreme INR Results
• Patients With Dose Changes

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a continuous primary outcome analyzed as a mean: percentage of time in therapeutic range over 12 months. It gives a group size, mean, and standard deviation for each arm, followed by a mean difference and confidence interval. These summaries allow a direct comparison of average time in range, while retaining information about variation in the outcome across participants.

What does the mean difference represent?

The comparison is expressed as the mean for 12-weekly monitoring relative to the 4-weekly arm. Its estimate is -2.5. Because the outcome is a percentage of time, the difference is on the scale of that percentage measure. The negative direction means the posted mean was lower in the 12-weekly arm. This is a group-level contrast; it does not state that every participant in that arm had a lower result.

In general, a mean difference summarizes the separation between two group averages in the original outcome units. It is distinct from a standardized effect size, which expresses a difference relative to variability. The registry also posts a standardized effect estimate of -0.129 and a pooled standard deviation of 19.4. Such standardized measures can help compare effects measured on different scales, but they are less directly interpretable clinically than the difference in the outcome’s own units.

Why report standard deviations?

In general, a standard deviation describes how dispersed individual measurements are around their group mean. The posted values are 18.8 for 4-weekly monitoring and 20.0 for 12-weekly monitoring. A standard deviation is not a confidence interval for the mean and does not describe the precision of the mean difference by itself. Precision also depends on how many participants contribute information and on the analysis method.

In general, over-dispersion means observed variation is greater than a model assumes. It can make standard errors too small if the model fails to account for that extra variation. That concern is especially relevant to some count or binary-data models; the primary endpoint is continuous, and the registry does not report a model-based diagnostic or an over-dispersion assessment. No inference about such a diagnostic should be made from the standard deviations alone.

How should the confidence interval and p-value be read?

In general, a confidence interval describes a range of values compatible with the data under the interval’s statistical method and assumptions. The primary interval runs from -7.313 to 2.313. It includes zero, so the posted interval does not isolate a single direction of difference. The registry does not identify the interval method or report adjusted inference. The unadjusted p-value is 0.309; a p-value measures how unusual results at least as incompatible with a null hypothesis would be under the assumptions of that test. It is not the probability that the null hypothesis is true, nor a measure of the clinical importance of the estimate.

The registry’s primary population is intention to treat. In general, intention-to-treat analysis aims to compare participants according to their randomized assignment, regardless of subsequent treatment adherence. This can preserve the randomized comparison, but the label alone does not explain how missing measurements were handled, what participants contributed to each endpoint calculation, or whether any additional analysis populations were used. Those details are not reported in the registry record.

What can secondary comparisons establish?

The posted secondary comparisons include binary outcomes, reported as numbers of participants and risk differences. In general, a risk difference contrasts the proportions experiencing an outcome between groups. The registry posts confidence intervals and unadjusted p-values for these comparisons. No adjusted secondary analyses are posted. Since these outcomes are secondary and no multiplicity strategy is described, an isolated unadjusted result should be treated as exploratory rather than as a definitive confirmatory finding.

The registry also lists major bleeding, extreme INR outcomes, and other measures that are not all represented in the posted secondary results. A listed outcome is not itself evidence that a result was observed or analyzed. The record does not report analysis details for the secondary outcomes beyond the posted summaries. The original statistical analysis plan, prespecified model specifications, assumptions, and any sensitivity analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean difference is -2.5, and its confidence interval extends from -7.313 to 2.313. The interval is broad enough to include zero and values in either direction. Thus, the point estimate alone does not convey the uncertainty: results compatible with the posted interval include a lower mean for 12-weekly monitoring, little or no difference, and a higher mean. The registry does not state a threshold for a clinically important difference, so the interval cannot be classified against such a threshold from the record.

In general, a confidence interval is a measure of statistical precision, not a guarantee that the true value lies within its endpoints. Its interpretation depends on the statistical method and assumptions used to construct it. The method is not reported in the registry record. The interval is for the mean difference, not for the range of individual participant outcomes; individual variation is reflected separately in the reported standard deviations.

The unadjusted p-value for the primary comparison is 0.309. In general, a larger p-value does not establish that the groups are equivalent, and a smaller p-value would not by itself establish clinical importance. Precision is better judged from the estimate and interval together, alongside a prespecified clinically meaningful threshold if one exists. No such threshold is reported in the registry record.

The posted arm sizes are 126 and 124, with standard deviations of 18.8 and 20.0. The registry does not provide missing-data details, a sensitivity analysis, or participant-level data that would help assess how robust the interval is to alternative assumptions. The primary outcome is explicitly identified as intention to treat, but that designation does not on its own resolve questions about incomplete outcome measurements.

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 the trial’s original design justification. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row plans for a stated fraction of the observed effect: 100%, 75%, or 50%. The primary outcome is continuous, and the posted planning quantities are participants per arm. The secondary dose-change illustration also gives participants per arm. The sample-size assumptions distinguish time-to-event calculations, which would give total events, but no such planning display is reported for these outcomes.

The 80% power column describes the number of participants per arm that the planning calculation would require for an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses the same idea with a higher target chance of detection. These are prospective planning concepts, not probabilities that the completed trial found an effect. The planning figures are not observed power.

Smaller effects require more participants to detect under otherwise unchanged assumptions. That is why the illustrations increase the planned per-arm sample size as the target fraction of the observed effect becomes smaller. These calculations should not be read as evidence that the original trial was designed around the observed effect: the trial’s own sample-size assumptions and justification are not reported in the registry record. The planning figures also depend on their stated approximation and allocation assumptions, and do not account for unreported design details or missing data.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -2.500; pooled standard deviation σ = 19.404.
2. n = 2 × (1.96 + 0.842)² × 19.404² / -2.500² = 945.7, rounded up to 946 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -2.5                      # observed difference in means
sigma <- 19.404439132954                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(356759)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 946 (80% power), 1,267 (90% power)
 75% of observed effect: n per arm = 1,682 (80% power), 2,251 (90% power)
 50% of observed effect: n per arm = 3,783 (80% power), 5,065 (90% power)
power.t.test: 946.7 
Simulated power at n = 946 per arm: 0.795 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies time in therapeutic range as the primary outcome and lists several secondary outcomes. The record reports no analysis entries for the trial and no reported analyses under the posted secondary outcomes. It does post summary comparisons for two secondary outcomes. The original statistical analysis plan, including any hierarchy among outcomes, is not reported in the registry record.

In general, multiplicity arises when several hypotheses are tested. If each is assessed without adjustment, the chance of at least one apparently notable result can rise as more tests are considered. Adjustment methods or a prespecified testing hierarchy can address this issue, but neither an adjustment method nor a hierarchy is reported in the registry record. The secondary p-values are unadjusted, so they should not be treated as if they were protected from the interpretive risk of multiple testing.

The registry names the intention-to-treat population for the primary outcome. In general, this approach analyzes participants according to randomized assignment and can preserve the intended randomized comparison. The record does not state how missing primary measurements were handled, whether all randomized participants had usable outcome data, or whether sensitivity analyses assessed alternative missing-data assumptions. It also does not identify analysis populations for the posted secondary outcomes.

Missingness can affect both the precision and interpretation of a result, particularly if availability of measurements is related to outcomes or treatment assignment. This is a general methodological concern, not evidence that missing data biased these results. The registry does not report the amount, timing, or reasons for any missing outcome information, so the extent of that concern cannot be determined from the record.

Further unreported details include the planned primary analysis model, the trial’s own significance threshold, any interim monitoring, and the handling of protocol deviations. Their absence limits reconstruction of the prespecified analysis and makes it important to distinguish posted registry summaries from a complete analysis report.

15. 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: cardiac death (2.4%), gastrointestinal bleeding (1.6%), respiratory failure (0.8%), septic shock (0.8%), renal infarct (0.8%).

The safety fields report participants affected by serious and other adverse events, alongside deaths, for each monitoring arm. For serious adverse events, the posted counts are 4 of 124 in the 12-weekly group and 7 of 126 in the 4-weekly group. For other adverse events, the counts are 7 of 124 and 4 of 126, respectively. Deaths are reported as 2 and 5. These are descriptive counts; the registry does not post confidence intervals or comparative statistical analyses for these safety fields.

The record also lists serious adverse-event terms with percentages: Cardiac death, 2.4%; Gastrointestinal bleeding, 1.6%; Respiratory failure, 0.8%; Septic shock, 0.8%; and Renal infarct, 0.8%. These entries do not establish how events were distributed across arms or whether participants experienced more than one event. The registry does not report additional detail about event timing, attribution, severity grading, or follow-up completeness. Counts should therefore be read as posted safety summaries, not as proof of a causal difference between monitoring schedules.

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

The trial estimates the average difference in percentage of time in therapeutic range between two warfarin-monitoring schedules in the enrolled stable-patient population over 12 months. The posted mean difference is -2.5 for 12-weekly relative to 4-weekly monitoring, with a confidence interval from -7.313 to 2.313. That interval includes zero and allows uncertainty in either direction. The result does not establish that the schedules are equivalent, because the registry does not report an equivalence or noninferiority margin or a design intended to test one.

The result also does not establish that either monitoring schedule is preferable for every participant. The group means conceal individual variation, and the posted standard deviations indicate that participant results varied within both arms. The record does not provide subgroup results, participant-level trajectories, or enough information to determine whether the average comparison applies equally across the listed conditions.

The secondary outcomes and adverse-event counts provide additional descriptive information, but they do not resolve the primary uncertainty. Some listed secondary measures have no posted results, and the analyses that are posted are unadjusted. The registry does not describe the multiplicity plan, missing-data handling, or full analysis strategy. These limits make it inappropriate to treat an isolated secondary result as definitive confirmation of a broad conclusion.

In general, a trial result is evidence about the population, outcome definitions, follow-up, and analysis actually studied. It is not a guarantee about outcomes outside that setting. The registry record concerns stable patients on long-term warfarin, compares the stated schedules, and reports the primary outcome at 12 months. Longer-term outcomes, detailed implementation, and results for populations not described in the record are not reported. The data should be understood as an estimate with uncertainty, rather than as a universal conclusion about monitoring frequency.

17. Why This Trial Matters Statistically

This trial addresses a statistical challenge that occurs when monitoring frequency is itself part of a clinical management strategy. A comparison of monitoring schedules needs to consider more than the number of contacts or tests: the primary endpoint captures the proportion of follow-up spent within a therapeutic range. That continuous measure can retain information about how much time is in range, while event outcomes represent different aspects of the clinical question.

The randomized parallel design provides a framework for comparing assigned schedules, and the registry identifies the primary analysis population as intention to treat. The reported arm means, standard deviations, and mean-difference interval allow readers to distinguish the estimated contrast from its uncertainty. The confidence interval is especially important: the point estimate alone might seem to favor one direction, but the interval includes zero and extends in both directions.

The record also illustrates why statistical significance and equivalence are not interchangeable. A p-value that does not provide strong evidence against a null hypothesis does not prove the schedules have the same outcome. Establishing equivalence would require a prespecified margin and analysis, neither of which is reported in the registry record. Planning calculations based on an observed effect likewise cannot replace the trial’s original design justification.

Finally, the difference between a named outcome and a posted analysis matters. Several secondary outcomes are listed, but only some have results, and the available secondary comparisons are unadjusted. Statistical interpretation depends not just on estimates but also on prespecification, multiplicity, missingness, and transparent reporting. The record’s limits make careful separation of observed summaries from broader conclusions particularly important.

18. 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 gives summary results but not participant-level data. This limits assessment of the distribution of time in therapeutic range, unusual observations, and variation in outcomes across participants. The primary outcome is described as calculated by linear interpolation, but further details of the calculation and the target range are not reported.

Although the primary population is identified as intention to treat, the record does not explain missing-data handling, report the completeness of primary outcome measurements, or provide sensitivity analyses. It also does not report subgroup analyses for the conditions listed. The results therefore cannot be assessed for robustness to alternative missing-data assumptions or compared across patient subgroups using this record alone.

The registry lists secondary outcomes that do not all have posted results. For those with posted comparisons, the p-values are unadjusted, and the multiplicity plan is not reported. The safety summary provides counts and selected serious adverse-event terms, but does not give comparative intervals, attribution, timing, or a detailed account of overlap between events and participants.

Other limitations in interpreting the design include the absence of the original sample-size justification, interim-analysis details, and a complete statistical analysis plan. The record also does not identify the roles covered by triple masking or provide further operational details about sham INR results. These are reporting limitations; the record alone does not establish that the procedures were inadequate or that the findings are biased.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prolongation of the Interval Between Monitoring of Warfarin in Stable Patients — NCT00356759.
• Registry record last updated 2018-08-22; status last verified 2018-08.
• Results first posted 2018-08-22.
• 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.

22. Record Summary

The registry describes a completed randomized, parallel-group, triple-masked phase 2 trial sponsored by Hamilton Health Sciences Corporation. It enrolled 250 participants and compared warfarin dose assessment every 4 weeks with assessment every 12 weeks in stable patients receiving long-term anticoagulation. The primary outcome was mean percentage of time in therapeutic range over 12 months, calculated by linear interpolation in the intention-to-treat population.

The posted primary mean difference was -2.5 for 12-weekly relative to 4-weekly monitoring, with a confidence interval from -7.313 to 2.313 and an unadjusted p-value of 0.309. The interval includes zero, leaving uncertainty about the direction and size of the average difference. Some secondary and safety summaries are posted, but not all listed outcomes have results. The original sample-size justification, complete statistical plan, and missing-data methods are not reported in the registry record.