Efficacy and Safety of Anticoagulant Therapy in Portal Vein Thrombosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Anticoagulant Therapy in Portal Vein Thrombosis (NCT04173429), a randomized phase 4 study. The primary outcome is Recanalization Rate.

2. Clinical Question

The registry describes a randomized controlled trial intended to evaluate the efficacy and safety of nadroparin calcium and warfarin in patients with portal vein thrombosis. Its primary outcome was the overall recanalization rate, including both complete and partial recanalization. A secondary outcome was rate of bleeding. The central statistical question is about the comparison between groups, not simply whether either group had recanalization: the size and precision of the difference matter when interpreting the posted counts.

The registry record identifies the population by the conditions liver cirrhosis and portal vein thrombosis. It does not report further eligibility details in the primary outcome entry. Nor does it report demographic or clinical characteristics in the information summarized for this analysis. Those missing details limit assessment of how closely the enrolled participants reflect any broader clinical population.

3. Trial Design

This was a phase 4, randomized, parallel-group trial with single masking. The registry lists an enrollment of 64 participants. The primary outcome results include 32 participants in each group. The identity of the masked party, the method used to generate the random allocation, and whether allocation was concealed are not reported in the registry record.

The intervention was sequential anticoagulation: nadroparin calcium every 12 hours for 1 month, followed by oral warfarin for 5 months. The comparator group received no anticoagulation therapy. The primary outcome and the secondary bleeding outcome both have a 6-month timeframe, corresponding to the treatment sequence described in the registry. The record does not specify whether outcome assessment continued beyond that timeframe.

The registry lists Qilu Hospital of Shandong University as sponsor. The recorded study start was 2017-01-01, and the primary completion date was 2020-01-31. The study status is completed. These registration details establish the broad trial structure and timing, but they do not supply the full protocol or a statistical analysis plan. Original sample-size assumptions, the intended analysis population, missing-data procedures, and interim-analysis plans are not reported in the registry record.

The posted primary outcome is a count of participants meeting the recanalization definition, rather than a continuous measurement of vein area or a time-to-event outcome. The registry also posts a count of participants with bleeding. The reported group counts allow a simple comparison of event proportions, but the record does not explain whether the analyses accounted for any factors beyond treatment group.

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

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 Recanalization Rate, measured over 6 months.

The primary endpoint is the overall recanalization rate at 6 months, reported as the number of participants with an outcome. It combines complete and partial recanalization. Complete recanalization was defined as complete disappearance of the thrombus in the portal vein trunk, at least one of the two intrahepatic portal vein branches, the superior mesenteric vein, and the splenic vein. Partial recanalization required a reduction of more than 50% in the thrombus, with no extension of the thrombus to other veins.

The registry describes measuring the vein and residual patent lumen at the level of maximum thrombosis. Total lumen area and patent lumen area were calculated using commercially available software, and thrombus occlusion was estimated from the ratio of thrombosis area to total lumen area. Those measurements underpin the classification, while the posted primary result is the count meeting either recanalization definition.

This endpoint is used to describe an anatomical change in portal venous thrombosis over the stated follow-up period. Combining complete and partial recanalization produces an overall outcome that includes more than complete disappearance of the thrombus. That combined definition should be kept in mind when interpreting the group comparison: the posted result does not separate the two forms of recanalization. The registry record does not report separate counts for complete and partial outcomes.

7. Results Posted in the Registry

• Nadroparin Calcium-warfarin Sequential Therapy Group: 62.5% (20/32) versus 34.4% (11/32) on control; risk difference 28.1 percentage points (95% CI 4.6 to 51.6), risk ratio 1.82 (1.05–3.15); unadjusted two-proportion z-test p = 0.024.

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.

Rate of Bleeding

• 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:
  • Nadroparin Calcium-warfarin Sequential (NWS) Therapy Group: 3.1% (1/32) versus 0.0% (0/32) on control; risk difference 3.1 percentage points (95% CI -2.9 to 9.2); unadjusted two-proportion z-test p = 0.313.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nadroparin Calcium-warfarin Sequential (NWS) Therapy Group and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: rate of bleeding at 6 months. Its overall pattern is sparse compared with the primary endpoint, with very few events recorded. This limits the amount of information the secondary outcome can contribute. The direction and uncertainty of its estimate do not provide a precise account of bleeding differences between groups.

The secondary endpoint addresses a different aspect of the trial from recanalization. The primary outcome concerns an anatomical change in thrombosis, while bleeding is a safety-related outcome. Reading them together provides a broader description of the outcomes recorded in the registry, but the secondary result does not confirm or overturn the primary comparison. Each outcome has its own event definition, data, and uncertainty.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis because they may be one of several outcomes examined and can be more vulnerable to chance findings. The registry record does not report a multiplicity plan, a hierarchy of outcome testing, or adjustments for multiple comparisons. It also does not report a detailed analysis plan. Consequently, the secondary finding should be treated as descriptive rather than as independent confirmatory evidence.

The record lists two outcome measures in total, including the primary and the bleeding endpoint, but does not give additional secondary analyses. No separate analyses are listed for different participant subgroups or for different bleeding definitions. Absence of such entries in the registry record does not establish that no analyses were conducted elsewhere; their results and methods are not reported in the registry record.

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

• Rate of Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion of participants with an event in one group with the proportion in another group. For this trial, the event is meeting the combined definition of complete or partial recanalization by 6 months. A positive risk difference in the direction used for the posted comparison means that the event proportion was higher in the sequential therapy group than in control. The measure is on an absolute scale, so it describes the difference between group proportions rather than a relative increase.

Why are there multiple effect measures?

The registry lists a risk difference, relative risk, and odds ratio for the primary outcome. Each summarizes the same binary outcome on a different scale. The risk difference focuses on the absolute contrast. The relative risk compares the proportions as a ratio. The odds ratio compares the odds of the outcome between groups. When outcomes are not rare, the odds ratio can look more extreme than the relative risk, so the measures should not be treated as numerically equivalent. The estimates and intervals are all summaries of the same observed group data, not separate trial findings.

What does the p-value contribute?

A p-value is a measure of how unusual data at least as discrepant as those observed would be under a specified null model and the test assumptions. It does not measure the probability that treatment has no effect, the probability that the observed result is due to chance, or the clinical value of the difference. A threshold-based reading can hide the distinction between evidence against a null comparison and the size or precision of an estimated effect. The p-value should therefore be considered together with the effect estimate, confidence interval, design, and limits of the registry record.

What does a confidence interval mean?

A confidence interval is a range produced by a statistical procedure that reflects uncertainty in an estimate. In repeated use under the procedure's assumptions, intervals constructed in this way would cover the underlying value at the stated confidence level at the corresponding frequency. For an individual study, the interval is not a guarantee that the true value lies inside it. Its width helps convey precision: a wider interval leaves a broader range of plausible values, while a narrower interval is more informative about the magnitude. The limits also depend on the analysis method and assumptions.

Why be cautious with a small binary-outcome trial?

Binary outcomes count whether each participant meets a definition or does not. When the group sizes and event counts are limited, the estimate can be sensitive to a small number of outcomes. Confidence intervals help make that uncertainty visible. The registry record does not describe any adjusted statistical model, so the posted comparison should not be interpreted as accounting for baseline characteristics or other covariates. It also does not provide the analysis method used to calculate the posted intervals and p-value.

How should the endpoint definition affect interpretation?

The primary endpoint combines complete and partial recanalization. A participant could therefore meet the endpoint through either of two different degrees of change. Since the record does not post separate counts for these categories, the overall result cannot establish how the observed outcomes were distributed between complete and partial recanalization. The operational definition specifies a greater than 50% reduction for partial recanalization and rules out extension to other veins. These criteria are part of the outcome itself, not merely statistical details.

What is over-dispersion, and is it relevant?

Over-dispersion is a general statistical concern when observed variability exceeds what a model assumes. It can make standard errors too small if the model does not account for the extra variability. The primary outcome is reported as a binary participant count, not as repeated counts or a rate with a person-time denominator. The registry record does not report a model for which over-dispersion adjustment can be assessed, so no such adjustment can be inferred.

What cannot be inferred from the record?

The registry record does not report the original sample-size justification, the planned statistical test, any interim analyses, an analysis-population definition, or missing-data methods. It also does not report the allocation-generation procedure, allocation concealment, or which party was masked. These omissions matter because they affect how fully the posted estimate can be connected to a prespecified plan. The registry lists no analysis entries, so the detailed conduct of the statistical analysis cannot be reconstructed from the record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.281, with a 95% confidence interval from 0.046 to 0.516. The interval is entirely on the positive side of zero, while spanning a range of possible effect magnitudes. That combination gives a direction for the estimated contrast but leaves uncertainty about its size. The interval is not so narrow that the point estimate should be treated as exact.

The relative risk is listed as 1.818, with interval limits 1.05 and 3.148. The odds ratio is 3.182, with interval limits 1.145 and 8.841. Their intervals also show uncertainty and are wider on their respective ratio scales. Because these measures express different contrasts, comparing their numerical magnitudes directly is not meaningful. The risk difference most directly conveys the absolute group separation.

Confidence intervals summarize sampling uncertainty under the calculation method and its assumptions. They do not address every source of uncertainty. The registry record does not report missing-data handling, the analysis population, or a detailed statistical method, so the intervals cannot resolve those questions. Nor do intervals account for unreported concerns such as departures from the planned analysis, if any. Precision is therefore only one part of judging how informative the posted result is.

The secondary bleeding estimate has a confidence interval that extends from -0.029 to 0.091 for the risk difference. Its interval includes zero and is compatible with a range of contrasts in either direction. This endpoint has only one reported event across the groups, so the posted estimate should be read as particularly limited in precision. The record does not report a separate precision analysis beyond the listed interval.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed primary effect, not the trial's original design calculations. For this binary-outcome comparison, each entry is the number of participants per arm, not a total across both groups and not a total number of events. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect.

For planning for 100% of the observed effect, the illustration lists 49 participants per arm for 80% power and 65 participants per arm for 90% power. For planning for 75% of the observed effect, it lists 87 participants per arm for 80% power and 115 participants per arm for 90% power. For planning for 50% of the observed effect, it lists 192 participants per arm for 80% power and 256 participants per arm for 90% power.

In plain language, power is the chance that a planned study would detect an effect of the specified size using the stated test threshold, if that effect were present and the assumptions held. The 80% and 90% columns represent two different target chances of detecting that effect. A higher target power requires more participants under the same assumptions. Likewise, planning to detect a smaller effect requires more participants, as the rows illustrate. The curve should be read as a planning aid under these assumptions, not as a reconstruction of the study's actual protocol calculations. These figures are not observed power.

The registry record does not report the trial's original sample-size justification or its planned effect size. These illustrations therefore cannot establish whether enrollment was adequate according to the investigators' original aims, nor whether the trial reached a prespecified target.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.344; treatment proportion p₁ = 0.625; average p̄ = 0.484.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7068 = 1.3852.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6782 = 0.5708.
4. n = (1.3852 + 0.5708)² / (0.2812)² = 48.4, rounded up to 49 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 <- 0.34375                          # control proportion
p1 <- 0.625                          # 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(4173429)
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 = 49 (80% power), 65 (90% power)
 75% of observed effect: n per arm = 87 (80% power), 115 (90% power)
 50% of observed effect: n per arm = 192 (80% power), 256 (90% power)
power.prop.test: 48.4 
Simulated power at n = 49 per arm: 0.817 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and one secondary outcome. It does not report a statistical plan for handling multiple outcomes or multiple comparisons. In general, repeated hypothesis tests can increase the chance of at least one apparently unusual result, even when no underlying differences exist. A prespecified testing hierarchy or multiplicity adjustment can address that issue, but whether either was planned or used is not reported in the registry record. The secondary result should therefore be interpreted cautiously and not treated as confirmatory on its own.

Missing-data procedures are not reported in the registry record. The posted primary results list 32 participants in each group, but the record does not explain whether all enrolled participants were assessed, whether any outcome values were missing, or how missing values would have been handled. The listed group counts alone do not define an intention-to-treat population or establish that every randomized participant contributed an outcome.

The analysis population is also not reported. The record does not specify whether the comparison used all randomized participants, participants who completed treatment, or another defined set. It does not describe exclusions after randomization, protocol deviations, or how adherence to the treatment sequence was considered. These details matter because the population included in an analysis can affect the interpretation of a randomized comparison.

The registry record lists no analysis entries. It does not describe a statistical analysis plan, planned covariate adjustment, interim analyses, or a prespecified approach to subgroup analyses. This leaves important aspects of analysis conduct unknown. The posted estimates can be described on their own terms, but the record does not allow a full assessment of whether those estimates correspond to prespecified procedures.

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 3.12% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event figures distinguish serious events, other reported events, and deaths. In the sequential therapy group, the registry records zero serious adverse events among 32 participants at risk, one other adverse event among 32 at risk, and zero deaths. In the control group, it records zero serious adverse events among 32 participants at risk, zero other adverse events among 32 at risk, and zero deaths.

These counts describe what is posted in the registry record; they do not establish that no other events occurred or that all events were captured. The record does not provide serious adverse-event terms, and no top serious-event terms are listed. It does not report event severity details for the other adverse event or a detailed method for collecting safety outcomes.

Zero recorded serious events in both groups does not show that the groups have identical safety profiles. With these group sizes and sparse event counts, the registry information offers limited precision for comparing uncommon harms. The separate secondary bleeding outcome should also be read as a distinct measure, not assumed to encompass every adverse event.

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

The primary result describes a higher observed count of participants meeting the combined recanalization definition in the sequential anticoagulation group than in the no-anticoagulation group. The listed risk difference and its confidence interval quantify the estimated group contrast and its uncertainty. The result is limited to the enrolled participants, the endpoint definition, and the 6-month timeframe recorded for this trial.

It does not establish that every participant would have the same outcome under either treatment assignment, nor does it identify the mechanism behind any observed difference. The registry provides no separate results for complete and partial recanalization, so the combined endpoint cannot show which category accounts for the group counts. It also does not report longer-term outcomes, which means the posted 6-month outcome cannot describe what happened after the stated timeframe.

The result does not by itself establish a broader effect across populations or clinical settings. The registry record does not provide detailed participant characteristics, eligibility criteria beyond the listed conditions, or an analysis of how outcomes vary across participant groups. The trial's enrollment was 64, and the precision limits should be considered when judging how much can be learned from its results.

The secondary bleeding information is sparse, and the adverse-event record is limited. Those data do not provide a precise comparison of uncommon safety outcomes. The absence of recorded serious events should not be interpreted as proof that serious harms cannot occur. Similarly, a statistical result for the primary outcome is not a complete assessment of the balance of outcomes.

Finally, the registry record does not report important analysis details, including missing-data handling, the analysis population, or a multiplicity plan. These omissions do not negate the posted counts, but they constrain how fully the statistical evidence can be evaluated. The appropriate reading is a description of the registered trial results with uncertainty, rather than a universal or definitive conclusion.

17. Why This Trial Matters Statistically

This trial illustrates why a binary clinical outcome should be interpreted through both its event counts and an effect estimate. Counts show how many participants met the endpoint in each group, while the risk difference expresses the absolute contrast. The confidence interval then shows that the estimated contrast has meaningful uncertainty. A p-value alone would not convey either the magnitude or the range of plausible values.

It also demonstrates the importance of outcome definitions. Recanalization combines complete disappearance of thrombus with a specified degree of partial reduction and no extension to other veins. Because the registry posts only the combined outcome, readers cannot determine how often each category occurred. Clear definitions help make results interpretable, but separately reported components can be important when a composite outcome includes events with different meanings.

The sample-size illustrations show how planning depends on the effect a future study aims to detect. Smaller target effects require more participants under the stated assumptions. Those calculations are distinct from the trial's actual design rationale, which is not reported in the registry record. Separating planning assumptions from observed results avoids treating a study's achieved sample as proof that it had a particular level of power.

Finally, the record highlights how statistical interpretation depends on reporting beyond the headline outcome. Details about allocation, masking, missing data, analysis populations, and multiplicity help readers assess the reliability and scope of a comparison. When such information is absent, the posted estimates remain describable, but their methodological context is incomplete.

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 limited information about who was eligible, participant characteristics, and the clinical setting beyond the listed conditions and sponsor. This makes it difficult to judge how representative the enrolled group may be. The identity of the masked party and the randomization and allocation-concealment procedures are also not reported.

The primary endpoint combines complete and partial recanalization, without separate counts for either category. The outcome is reported at 6 months, and no longer follow-up results are listed. The record does not report whether outcome assessment was blinded or how consistently the imaging measurements and classifications were applied.

The analysis details are incomplete. The record does not report the original sample-size rationale, statistical analysis plan, analysis population, missing-data methods, or any interim analyses. It also does not describe a multiplicity strategy. These omissions limit assessment of whether the posted comparisons follow prespecified procedures and how robust they are to alternative analytic choices.

Safety information is sparse. No serious adverse events or deaths are recorded in either group, while the counts of other adverse events are limited. The registry provides no serious-event terms and little detail about the nature or ascertainment of non-serious events. Consequently, the available safety counts cannot precisely characterize uncommon outcomes.

These limitations concern what the registry record reports. They do not show that the omitted procedures were absent from the trial; those details are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Anticoagulant Therapy in Portal Vein Thrombosis — NCT04173429.
• Registry record last updated 2021-03-02; status last verified 2017-01.
• Results first posted 2021-03-02.
• 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.

22. Record Summary

The registry describes a completed phase 4 randomized, single-masked, parallel-group trial of sequential nadroparin calcium and warfarin versus no anticoagulation in patients with liver cirrhosis and portal vein thrombosis. Enrollment was 64. The primary outcome was overall complete or partial recanalization at 6 months, and the listed secondary outcome was bleeding rate at 6 months.

The posted primary counts were 20 of 32 in the sequential therapy group and 11 of 32 in control. The listed risk difference was 0.281, with a 95% confidence interval from 0.046 to 0.516 and an unadjusted p-value of 0.024. The registry also records sparse bleeding and adverse-event data. Analysis populations, missing-data procedures, multiplicity handling, and the original sample-size justification are not reported in the registry record.