Phase 2 Study of Rivaroxaban Reversal by Ciraparantag as Measured by WBCT: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 2 Study of Rivaroxaban Reversal by Ciraparantag as Measured by WBCT (NCT03172910), a randomized phase 2 study. The primary outcome is Subjects Achieving Complete Reversal of Anticoagulation (WBCT is ≤ 110% of Baseline).

2. Clinical Question

3. Trial Design

This was a randomized, single-blind, placebo-controlled, single-site phase 2 study, with a sequential model recorded in the registry. Its stated purpose was to assess the efficacy and safety of ciraparantag in healthy volunteers anticoagulated with rivaroxaban, using whole blood clotting time (WBCT). The registry record lists enrollment of 69 and a completed status.

The arms were placebo and ciraparantag at 30 mg, 60 mg, 120 mg, and 180 mg. The posted primary-outcome counts are 3 of 16 for placebo, 7 of 12 for 30 mg, 11 of 12 for 60 mg, 11 of 12 for 120 mg, and 12 of 12 for 180 mg. The safety record also includes an “Enrolled Not Randomized” group; its safety information should not be confused with the primary-outcome comparisons.

The registry record gives a study start of 2017-05-08 and a primary completion date of 2019-11-12. It does not report the randomization procedure, the sequence of cohort enrollment or dose escalation, allocation concealment, or which study personnel or participants were blinded. The title identifies the study as single-site, but the site name is not reported in the registry record. Protocol details beyond the brief description, including administration timing and the schedule of WBCT measurements, are not reported in the registry record.

The primary endpoint was assessed within 1 hour. The analysis population was defined by receipt of study drug, at least one on-treatment WBCT measurement, and the absence of protocol deviations considered capable of affecting the measurements. The registry record does not give arm-specific counts for this defined population beyond the posted endpoint counts and denominators.

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: 69 subjects enrolled; 64 subjects were randomized and 5 subjects were not randomized. Of the 5 subjects not randomized, 2 did not achieve a sufficient level of anticoagulation per protocol, 1 was withdrawn by Investigator decision (due to an asymptomatic low heart rate), 1 subject withdrew consent, and 1 had an AE during the rivaroxaban administration period causing discontinuation (T wave inversion observed on ECG).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Pharmacodynamic population: all subjects who receive administration of study drug and provide at least one on-treatment whole blood clotting time measurement without protocol deviations with potential to affect these measurements.

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: A total of 69 subjects were enrolled, and all of these subjects received at least 1 dose of rivaroxaban. Of these 69 subjects, 5 were not randomized, did not receive study drug (ciraparantag or placebo), and were discontinued from the study.

6. Primary Endpoint

The registry lists the primary outcome as Subjects Achieving Complete Reversal of Anticoagulation (WBCT is ≤ 110% of Baseline), measured over Within 1 Hour.

The primary endpoint counted participants who achieved complete reversal of anticoagulation according to a WBCT criterion. A participant met the endpoint if manual WBCT was at most 110% of baseline at any post-baseline time point up to and including 1 hour after ciraparantag or placebo administration. Thus, the endpoint is a binary classification: each participant either met the criterion within the stated window or did not.

WBCT is a laboratory measure of clotting time. A baseline-relative threshold gives the endpoint a defined reference point for each participant, while the time window specifies when a qualifying measurement had to occur. The registry describes the endpoint as pharmacodynamic, so it reflects a measured clotting-time response rather than a clinical outcome such as bleeding, transfusion, or thrombosis. Those clinical outcomes are not reported as primary outcomes in this record.

Using a participant count makes the endpoint straightforward to interpret: the posted result gives the number meeting the criterion within each arm, alongside its denominator. It does not show the full timing or magnitude of each participant’s WBCT measurements, nor how long any change persisted beyond the assessment window. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Ciraparantag 30 mg: 58.3% (7/12) versus 18.8% (3/16) on control; risk difference 39.6 percentage points (95% CI 5.8 to 73.4), risk ratio 3.11 (1.01–9.60); unadjusted two-proportion z-test p = 0.031.
• Ciraparantag 60 mg: 91.7% (11/12) versus 18.8% (3/16) on control; risk difference 72.9 percentage points (95% CI 48.2 to 97.6), risk ratio 4.89 (1.74–13.75); unadjusted two-proportion z-test p = <0.001.
• Ciraparantag 120 mg: 91.7% (11/12) versus 18.8% (3/16) on control; risk difference 72.9 percentage points (95% CI 48.2 to 97.6), risk ratio 4.89 (1.74–13.75); unadjusted two-proportion z-test p = <0.001.
• Ciraparantag 180 mg: 100.0% (12/12) versus 18.8% (3/16) on control; risk difference 81.2 percentage points (95% CI 62.1 to 100.4), risk ratio 5.33 (1.92–14.79); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: the registry reports the number of participants who met the WBCT criterion in each arm. For a binary outcome, a group’s observed count is interpreted alongside its denominator. A count on its own does not express how common the outcome was in the group, while the denominator provides the context for the count. The posted arm counts and denominators allow the reported comparisons to be read in that context.

What does a risk difference express?

A risk difference compares the proportion meeting the endpoint in a ciraparantag arm with the proportion in the placebo arm by subtraction. Positive values indicate a larger observed proportion in the ciraparantag arm. The posted risk difference estimates are 0.396 for 30 mg, 0.729 for 60 mg, 0.729 for 120 mg, and 0.812 for 180 mg. They are unadjusted comparisons based on the observed arm summaries. They do not adjust for other variables, and the registry record does not report an adjusted model.

The risk difference is often useful because it expresses the contrast on the outcome’s proportion scale. General statistical interpretation: it describes the absolute separation between the groups’ observed proportions, whereas a ratio describes their relative relationship. Because the outcome is a participant count, the risk difference concerns the likelihood of meeting the WBCT threshold, not the size of a change in clotting time.

How do risk ratios and odds ratios differ?

A risk ratio compares the proportions meeting the endpoint in two groups as a ratio. Values above 1 correspond to a higher observed proportion in the ciraparantag group than in placebo. The registry reports risk ratios for each dose comparison, with confidence intervals. An odds ratio instead compares the odds of meeting the endpoint between groups. Odds and proportions are related but are not interchangeable, particularly when the outcome is common. The registry reports odds ratios for 30 mg, 60 mg, and 120 mg; an odds ratio for 180 mg is not reported in the posted comparison results.

These measures answer related but different questions. None replaces inspection of the actual counts and denominators. In particular, ratio estimates may look large when the placebo proportion is relatively low, while confidence intervals show how uncertain the estimated ratio remains. General statistical explanation: a ratio’s null value is 1, while the null value for a risk difference is 0.

What does a p-value tell the reader?

The posted p-values are unadjusted: 0.031 for 30 mg and <0.001 for 60 mg, 120 mg, and 180 mg. A p-value describes how compatible the observed data are with a specified null model, assuming that model and the analysis method are appropriate. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of the observed difference. The record does not identify the test or model used to produce these values, so the method should not be inferred from the p-values alone.

Because each dose is compared with placebo, there are multiple comparisons. General statistical explanation: when many tests are considered, the chance of at least one apparently unusual result can increase unless the analysis addresses multiplicity. No multiplicity method or prespecified testing hierarchy is reported in the registry record. The p-values should therefore be read as unadjusted comparisons, not as multiplicity-controlled evidence.

Why does the analysis population matter?

The registry defines a pharmacodynamic population consisting of participants who received study drug and contributed at least one on-treatment WBCT measurement, with protocol deviations that could affect those measurements excluded. This definition focuses the endpoint analysis on participants with usable pharmacodynamic measurements under the registry’s stated criteria. The record does not report how many participants were excluded for missing measurements or protocol deviations, or whether other analysis populations were used. It also does not describe imputation or other missing-data procedures.

General statistical explanation: excluding participants can change the population represented by an estimate, especially if the reason for exclusion is related to treatment or outcome. The stated population definition is therefore relevant when interpreting the endpoint counts. It should not be silently treated as an intention-to-treat analysis, because that label and its implementation are not reported.

What can be inferred from the posted comparisons?

The calculations are unadjusted comparisons of the posted summaries. They describe differences between the randomized study arms as recorded, but do not provide adjustment for baseline factors or model-based estimates of a dose trend. The trial is described as sequential, yet details of cohort timing and whether comparisons were concurrent are not reported. That information matters when assessing how the arm comparisons were conducted and whether changes over time could be relevant.

General statistical explanation: small samples can yield unstable estimates, and a few participant outcomes can have a substantial influence on a group proportion. Confidence intervals express uncertainty around an estimate, but their width and coverage depend on the method used. The registry record does not report the confidence-interval method, test method, statistical software, or the complete analysis plan. Those methods should not be reconstructed from the displayed values.

10. Confidence Intervals and Precision

The confidence intervals indicate that the estimated contrasts are uncertain, even where the posted point estimates are sizeable. For 30 mg, the risk difference is 0.396, with a confidence interval from 0.058 to 0.734. For 60 mg and 120 mg, each estimate is 0.729, with an interval from 0.482 to 0.976. For 180 mg, the estimate is 0.812, with an interval from 0.621 to 1.004. These ranges represent uncertainty in the estimated risk difference, not a range of individual participants’ outcomes.

General statistical explanation: a confidence interval gives a range of values compatible with the data under the interval method and its assumptions. A wider interval generally means less precision. It does not mean that each value in the range is equally likely, and it does not capture every source of uncertainty, such as limitations in the design or outcome definition.

The risk-ratio intervals are also broad: 1.008 to 9.597 for 30 mg, 1.738 to 13.75 for both 60 mg and 120 mg, and 1.923 to 14.79 for 180 mg. They show that the estimated relative contrasts are not tightly pinned down. The 30 mg interval’s lower limit is close to the null value of 1, while the higher-dose intervals also span a wide range of possible relative effects.

The 180 mg risk-difference interval reaches 1.004, beyond the possible upper bound of a risk difference. This can occur with an interval procedure that does not constrain estimates to the parameter’s feasible range. The registry record does not report the interval method, so the reason for this specific boundary behavior cannot be established from the posted information. The interval should be interpreted as a signal of estimation uncertainty, not as a feasible risk difference above the maximum.

These intervals reflect sampling uncertainty under the analysis, not uncertainty about whether the endpoint is clinically meaningful or applies to patients. The small denominators in the arms and the selected pharmacodynamic population are important context for precision and generalizability.

11. 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 participants per arm, not total events. They are illustrations based on the observed effect, not a report of the trial’s original design calculation. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned participants per arm under those assumptions for a design intended to have an 80% chance of detecting the specified effect if that effect is present. The 90% power column gives the corresponding per-arm planning figure for a design targeting 90% power. These are planning quantities, not observed results from the completed study. They are not observed power.

The rows describe planning for 100%, 75%, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so it requires more participants under the same assumptions. For example, the 60 mg comparison has planning figures of 6 and 8 participants per arm for 80% and 90% power when planning for the full observed effect, and 27 and 35 participants per arm when planning for 50% of that effect. The 30 mg and 120 mg comparisons also have planning figures; a corresponding planning row for 180 mg is not reported in the registry record.

These illustrations inherit the uncertainty of the observed effect used to generate them. If that observed difference is unstable, the resulting planning numbers may not be a dependable guide for a future study. They should be interpreted as scenario calculations under the stated assumptions, not as a validated design recommendation or as evidence about the power achieved by this trial.

12. 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 = 0.188; treatment proportion p₁ = 0.583; average p̄ = 0.385.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6883 = 1.3490.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6288 = 0.5292.
4. n = (1.3490 + 0.5292)² / (0.3958)² = 22.5, rounded up to 23 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 <- 0.1875                          # control proportion
p1 <- 0.583333333333333                          # 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(3172910)
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 = 23 (80% power), 30 (90% power)
 75% of observed effect: n per arm = 39 (80% power), 52 (90% power)
 50% of observed effect: n per arm = 81 (80% power), 108 (90% power)
power.prop.test: 22.5 
Simulated power at n = 23 per arm: 0.813 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry posts a primary endpoint and no secondary outcomes. It also records no posted analyses in the analysis field. The outcome summaries include comparisons of four ciraparantag dose groups with placebo, each with an unadjusted p-value. A multiplicity adjustment, testing hierarchy, or other family-wise error strategy is not reported in the registry record. Consequently, the p-values should be interpreted as unadjusted rather than as results from a reported multiplicity-controlled analysis.

The primary endpoint population is described as participants who received study drug and had at least one on-treatment WBCT measurement, excluding protocol deviations with potential to affect those measurements. The registry record does not report the number excluded under this definition, the handling of missing measurements, or whether any imputation or sensitivity analyses were performed. It does not state whether the posted arm denominators represent all randomized participants or only those meeting the pharmacodynamic population definition.

The record does not report an intention-to-treat analysis, a per-protocol analysis, or other named analysis populations. Nor does it give details of protocol deviations by arm. The stated population definition should therefore be used when reading the outcome, without assuming an unreported population or missing-data method.

Interim analyses, stopping rules, and the original statistical analysis plan are not reported in the registry record. The sequential model is recorded, but the cohort sequence and any rules governing advancement between cohorts are not described. Without those details, the potential implications of sequential enrollment for the comparisons cannot be fully assessed. The original design’s sample-size rationale and its planned handling of multiple comparisons are also not reported.

14. 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: supraventricular tachycardia (8.3%).

The safety record lists serious adverse events for the placebo and ciraparantag groups, as well as a group labeled “Enrolled Not Randomized.” No serious adverse events are listed for placebo, 30 mg, 60 mg, or 120 mg. One serious adverse event is listed for 180 mg. No deaths are listed in any group. The record lists supraventricular tachycardia as the top serious event term, at 8.3%.

Other adverse events are recorded for 3 participants in the placebo group, none in the 30 mg group, 2 in the 60 mg group, 8 in the 120 mg group, and 10 in the 180 mg group. The “Enrolled Not Randomized” group has 1 other adverse event listed. These are descriptive counts; the registry record does not provide event-level detail, severity breakdowns for these other events, or a statistical comparison of safety outcomes.

Safety counts should be read separately from the primary WBCT endpoint. The safety record includes a group that is not one of the randomized treatment arms used in the endpoint comparisons. The registry record does not establish from these summaries whether the serious event term corresponds to the listed serious event in the 180 mg group. Absence of a listed event is not proof that no risk exists.

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

The posted results describe how often healthy volunteers anticoagulated with rivaroxaban met a specific WBCT threshold within the study’s 1-hour assessment window. The counts were higher in each ciraparantag group than in the placebo group in this record. The unadjusted risk-difference estimates and their confidence intervals quantify those observed arm contrasts, while the p-values summarize unadjusted statistical comparisons.

The endpoint is a laboratory measure, not a direct measure of clinical benefit. Meeting the WBCT threshold does not, by itself, establish that bleeding is prevented, that an urgent procedure can be performed safely, or that patient outcomes improve. The registry record does not report those clinical outcomes as the primary endpoint. It also does not provide evidence from patients who need reversal treatment; the population described is healthy volunteers.

The results do not determine which dose should be used or whether any dose is appropriate for a particular person. They are not medical advice. They also do not establish the durability of the WBCT response beyond the stated assessment window, because follow-up for this endpoint is described only as within 1 hour. The registry record does not report how the measured response relates to later clotting, bleeding, or other clinical events.

Interpretation is further limited by the small arm denominators, the analysis population definition, and the unadjusted nature of the posted comparisons. The registry record does not report a multiplicity strategy, the confidence-interval method, or the detailed statistical plan. The sequential design is identified, but its implementation is not described in enough detail to evaluate cohort timing. The observed pattern is therefore best understood as a preliminary pharmacodynamic finding in the population and setting described, not as a definitive estimate of clinical effects.

16. Why This Trial Matters Statistically

This study illustrates how a trial can use a measurable laboratory endpoint to examine a pharmacodynamic response. The primary outcome was not simply a change in WBCT; it classified participants according to whether their manual measurement reached a prespecified baseline-relative threshold within a defined period. That choice makes the endpoint interpretable as a participant count, while also narrowing what the result can say.

The posted counts make the small-sample issue visible. For example, the placebo group had 3 participants meeting the threshold out of 16, compared with 12 of 12 in the 180 mg group. Such counts may produce sizeable point estimates, but small denominators can leave substantial uncertainty about the underlying contrast. The confidence intervals are therefore essential context, not an optional technical detail.

The dose comparisons also show why multiplicity matters. Several doses are compared with the same placebo group, and the posted p-values are unadjusted. A reader who focuses only on the p-values may overlook that the registry record does not report a strategy for handling multiple comparisons. The estimates and intervals provide more information about magnitude and precision, while still requiring caution about the analysis and design details that are not reported.

Finally, this record separates pharmacodynamic evidence from clinical outcomes. A laboratory response can be informative for understanding a mechanism or planning further research, but it cannot stand in for patient-centered outcomes without supporting evidence. The healthy-volunteer population, single-site setting, and brief endpoint window define the scope of these findings. The registry record is useful statistically because it makes those distinctions—and the limits of the available analysis—important to keep in view.

17. 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 population consisted of healthy volunteers anticoagulated with rivaroxaban, rather than patients receiving anticoagulation for a clinical condition. This limits how directly the endpoint results can be applied to patient care. The primary outcome was a pharmacodynamic measure based on manual WBCT and a baseline-relative threshold, not a clinical endpoint. The follow-up window for the primary outcome extended only to 1 hour.

The arms have small denominators, and the confidence intervals show considerable uncertainty in the estimated contrasts. The 180 mg risk-difference interval extends to 1.004, beyond the parameter’s feasible upper limit. The registry record does not report the method used to construct confidence intervals, so the behavior of that interval cannot be assessed further.

The study is described as sequential, randomized, single-blind, and single-site, but key implementation details are not reported. These include cohort timing, the randomization method, who was blinded, allocation concealment, and any dose progression rules. The sequential structure makes cohort timing particularly relevant to interpreting dose comparisons, but it cannot be evaluated from the posted record.

The analysis population excludes participants with certain protocol deviations and requires an on-treatment WBCT measurement. The registry record does not report exclusions by arm, missing-data procedures, or sensitivity analyses. It also does not report multiplicity adjustment for the dose-versus-placebo comparisons. These omissions limit assessment of selection, missingness, and the uncertainty associated with multiple tests.

Finally, details needed to reproduce the analysis—including the test used for p-values, interval method, full analysis plan, and original sample-size rationale—are not reported in the registry record. Safety summaries are counts and do not provide enough detail to assess event timing, seriousness beyond the serious-event listing, or comparative safety statistically.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Phase 2 Study of Rivaroxaban Reversal by Ciraparantag as Measured by WBCT — NCT03172910.
• Registry record last updated 2025-09-02; status last verified 2025-08.
• Results first posted 2025-09-02.
• 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.

21. Record Summary

The registry record describes a completed, randomized, single-blind, placebo-controlled, single-site phase 2 study with a sequential model. It evaluated ciraparantag in healthy volunteers anticoagulated with rivaroxaban, using manual WBCT to assess complete reversal within 1 hour.

The primary endpoint counts were 3 of 16 for placebo, 7 of 12 for 30 mg, 11 of 12 for 60 mg, 11 of 12 for 120 mg, and 12 of 12 for 180 mg. Unadjusted risk differences versus placebo were posted with confidence intervals and p-values. The record also includes serious and other adverse-event counts, with no deaths listed.

The findings concern a short-window laboratory endpoint in the stated population. The registry record does not report clinical outcomes, a multiplicity strategy, missing-data methods, or detailed statistical procedures.