Heparin Prophylaxis Dosing for Antepartum Hospitalizations (HEPDOSE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Heparin Prophylaxis Dosing for Antepartum Hospitalizations (HEPDOSE) (NCT04635839), a randomized phase 4 study. The primary outcome is Number of Participants With Elevated Serum Activated Partial Thromboplastin Time Above the Normal Range (> 36.2 Seconds)..

2. Clinical Question

The trial also sought to assess receipt of neuraxial anesthesia and pregnancy outcomes, and to evaluate unfractionated heparin pharmacokinetics and pharmacodynamics in pregnancy. The primary posted result concerns an elevated laboratory measurement, rather than a direct comparison of anesthesia eligibility or a clinical outcome. This distinction matters when interpreting the result: a difference in the surrogate endpoint describes a difference in the recorded laboratory outcome, and does not by itself establish a difference in anesthesia decisions or pregnancy outcomes.

3. Trial Design

The registry describes HEPDOSE as a phase 4 randomized controlled trial with a parallel-group design and no masking. It compared standard dosing of unfractionated heparin with dosing based on gestational age for thromboprophylaxis among hospitalized antepartum patients. The sponsor is the University of California, Los Angeles. The registry lists enrollment as 46, a start date of 2020-12-15, primary completion on 2022-03-31, and status as completed.

The posted primary outcome counts are 1 participant in the Standard Dosing group and 8 participants in the Gestational Age-Based Dosing group. The corresponding group denominators for this outcome are 21 and 24. The registry enrollment field and the primary-outcome denominators are not identical in presentation; the registry record does not explain the relationship between them or report a participant disposition accounting for it. The outcome-specific denominators should therefore be used when reading the primary comparison.

Random allocation is intended, in general, to reduce systematic differences in baseline characteristics between treatment groups. It does not guarantee that groups will be alike in every respect, particularly when the amount of information is limited. The record says that masking was none, but does not describe who knew the assigned dosing strategy or whether outcome assessment was masked. It also does not report details of the randomization sequence, allocation concealment, study sites, eligibility criteria, or the original design assumptions for the trial's sample size.

The treatment contrast is between dosing strategies, not between unfractionated heparin and no prophylaxis. The registry's description indicates that both groups received unfractionated heparin. The posted record does not provide dosing schedules, adherence information, treatment changes, or the clinical characteristics needed to assess how broadly the results apply beyond the enrolled population.

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:

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 Number of Participants With Elevated Serum Activated Partial Thromboplastin Time Above the Normal Range (> 36.2 Seconds)., measured over Collected 6 hours after unfractionated heparin dose until patient was taken of unfractionated heparin, an average of 1 week.

The primary endpoint is the number of participants with serum activated partial thromboplastin time above the normal range, defined in the registry title as > 36.2 seconds. Measurements were collected 6 hours after an unfractionated heparin dose and continued until the patient was taken off unfractionated heparin; the timeframe is described as an average of 1 week.

The registry characterizes this laboratory measure as a surrogate marker for whether a patient would be eligible for neuraxial anesthesia under guidelines for pregnant women receiving VTE prophylaxis. A surrogate is an intermediate measurement used to represent an aspect of a clinical process, rather than the clinical event or decision itself. In this trial, the primary endpoint therefore concerns the laboratory threshold. It does not directly count participants who did or did not receive neuraxial anesthesia, nor does it establish the reason for an anesthesia decision.

For the primary comparison, the posted counts are 1 of 21 in the Standard Dosing group and 8 of 24 in the Gestational Age-Based Dosing group. The statistical comparison estimates the difference in the proportions meeting the threshold. Interpretation should keep the endpoint's role in view: it may inform a question about a laboratory marker associated with anesthesia eligibility, but the registry record does not establish how closely this marker corresponded to actual eligibility or anesthesia practice in the trial.

7. Results Posted in the Registry

• Gestational Age-Based Dosing: 33.3% (8/24) versus 4.8% (1/21) on control; risk difference 28.6 percentage points (95% CI 7.6 to 49.5), risk ratio 7.00 (0.95–51.45); unadjusted two-proportion z-test p = 0.017.

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.

Number of Participants Diagnosed With Venous Thromboembolism (Pulmonary Embolism and/or Deep Venous Thromboembolism)

• 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:
  • Gestational Age-Based Dosing: 0.0% (0/24) versus 4.8% (1/21) on control; risk difference -4.8 percentage points (95% CI -13.9 to 4.3); unadjusted two-proportion z-test p = 0.280.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Gestational Age-Based Dosing and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants That Received General Anesthesia

• 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:
  • Gestational Age-Based Dosing: 0.0% (0/24) versus 4.8% (1/21) on control; risk difference -4.8 percentage points (95% CI -13.9 to 4.3); unadjusted two-proportion z-test p = 0.280.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Gestational Age-Based Dosing and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants That Received a Blood Transfusion

• 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:
  • Gestational Age-Based Dosing: 29.2% (7/24) versus 5.0% (1/20) on control; risk difference 24.2 percentage points (95% CI 3.6 to 44.7), risk ratio 5.83 (0.78–43.51); unadjusted two-proportion z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Gestational Age-Based Dosing than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address several different questions: venous thromboembolism, anesthesia use and timing, delivery, blood loss, transfusion, and anti-factor Xa level. Together they add clinical and pharmacologic context to the primary laboratory endpoint, but they do not measure the same thing. A laboratory threshold intended as a surrogate for anesthesia eligibility cannot stand in for actual anesthesia receipt, and neither measure alone captures the full range of pregnancy outcomes.

The posted numerical comparisons do not show a uniform direction across the secondary outcomes with results. For some comparisons, the observed event count is lower in the gestational age-based group; for another, it is higher. This mixed pattern is a reason to avoid describing the secondary findings as a consistent overall advantage or disadvantage. The results for several other listed outcomes are not reported in the registry record, so the broader set of planned clinical and pharmacologic questions cannot be evaluated from the posted numerical data.

Secondary results generally carry less weight than a well-specified primary analysis because they may be less central to the study question, may have fewer events, and may be among many comparisons. Each unadjusted test is interpreted without an adjustment for the number of outcomes examined. If many outcomes are considered, some can appear unusual through chance alone. The record does not report a multiplicity plan or identify an adjusted set of secondary analyses.

These outcomes are best treated as descriptive and exploratory in the absence of more information about prespecification, analysis populations, and multiplicity. Their role is to help identify questions for further evaluation, not to override the primary endpoint or to establish broad conclusions about clinical outcomes. The registry record does not provide enough detail to determine whether every listed secondary outcome was analyzed or how unposted results should be interpreted.

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

• Number of Participants Diagnosed With Venous Thromboembolism (Pulmonary Embolism and/or Deep Venous Thromboembolism)
• Number of Participants Who Did Not Receive or Had a Delay of Neuraxial Anesthesia Due to Unfractionated Heparin
• Number of Participants That Received General Anesthesia
• Number of Participants That Had a Delay in Timing of Delivery Due to Unfractionated Heparin
• Maximum Anti-Factor Xa Level Measured
• Mode of Delivery
• Estimated Blood Loss From Delivery
• Number of Participants That Received a Blood Transfusion

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, each participant either meets the defined event condition or does not. The primary result is reported as a count of participants with elevated activated partial thromboplastin time and as a comparison of the event proportions in the randomized groups. Counts make the observed data concrete, while a risk difference expresses the contrast between the proportions on an absolute scale. The reported primary risk difference is 0.286 for gestational age-based dosing compared with standard dosing.

What does the risk difference describe?

The risk difference is the proportion with the endpoint in the gestational age-based group minus the proportion in the standard-dosing group. A positive value means the observed proportion was higher in the first group. The posted group proportions are 0.333 and 0.048, respectively, and the reported risk difference is 0.286. These quantities are based on the outcome-specific group denominators, not on the enrollment field alone. The difference is an absolute contrast; it is not a relative risk and should not be described as a percentage increase.

In general, an absolute measure is useful because it describes the size of the observed separation on the event-proportion scale. A relative measure instead compares one proportion with another as a ratio. The registry also posts relative risk and odds ratio estimates for the primary outcome, but their confidence intervals are broad. Relative measures can be especially unstable when event counts are limited, so they should be read alongside the observed counts and the absolute risk difference rather than in isolation.

What does the confidence interval add?

A confidence interval describes the uncertainty around an estimated effect under the method used to construct it. It is not a range that guarantees the true effect lies inside it, and it does not describe the spread of individual laboratory values. The primary risk-difference interval runs from 0.076 to 0.495. Because the interval does not include zero, its range is compatible with a positive difference under the reported comparison. Its width also indicates that the estimate is not precise enough to identify a narrowly defined effect size.

The registry does not identify the confidence-interval construction method, so the interval should not be attributed to a particular formula or model. The same caution applies to the unadjusted p value of 0.017: the registry posts the value but does not name the statistical test or provide a detailed analysis plan. No adjusted primary analysis is reported in the record.

Why do event counts matter?

With a binary endpoint and relatively few observed events, changing the classification of a participant can materially affect the estimated group proportions. This general property makes the underlying counts important context for the estimate. The interval captures some sampling uncertainty, but it does not account for every possible source of uncertainty, such as outcome misclassification, differences in clinical practice, or limitations in how the participants were selected. The registry record does not report enough detail to assess those issues fully.

There is no reported continuous distribution for the primary measurement, such as individual activated partial thromboplastin time values or a mean and standard deviation. The posted analysis instead classifies participants according to whether the measurement crossed the stated normal-range threshold. As a result, the comparison cannot reveal how far above or below the threshold individual measurements were, or whether values clustered near the cutoff.

What does unadjusted mean?

An unadjusted comparison uses the posted group results without accounting for additional covariates or other comparisons. This is a direct way to describe the observed randomized-group contrast, but it does not show whether an adjusted analysis would give the same estimate. The registry record does not report covariate adjustment, an analysis population such as intention-to-treat, or how missing outcome data were handled. Those elements should not be inferred from the presence of randomized allocation.

More generally, randomized allocation supports a comparison of assigned groups, but analysis decisions still matter. Excluding participants, analyzing them according to treatment received rather than assigned, or handling missing observations differently can change the meaning of a result. The posted record does not give the information needed to determine whether any such choices were made. The outcome-specific denominators are reported, but reasons for those denominators are not.

How should the secondary comparisons be read?

The posted secondary comparisons are also unadjusted. Each outcome addresses a different aspect of the study, such as venous thromboembolism, general anesthesia, or transfusion. A confidence interval for a secondary risk difference describes uncertainty for that particular comparison; it does not address the combined chance of observing a notable result among many outcomes. When several outcomes are examined, chance variation can make some unadjusted findings appear more striking than they would in a prespecified, multiplicity-controlled analysis. The registry record does not report whether any outcomes were designated in advance beyond the listed primary endpoint or whether a multiplicity procedure was planned.

Statistical significance should not replace attention to the clinical meaning of each endpoint, the size and uncertainty of the estimate, and whether the analysis was prespecified. In particular, a surrogate laboratory outcome and a clinical outcome do not answer the same question. The methods information in the registry is not sufficient to reconstruct the full analysis plan, and no test choice, model specification, or missing-data procedure should be assumed.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.286, with a 95% confidence interval from 0.076 to 0.495. The interval lies above zero, but it is wide: the data are compatible with effects ranging from a comparatively smaller positive difference to a considerably larger one. This is a useful distinction between direction and precision. The interval supports a positive observed contrast under the reported method, while leaving substantial uncertainty about its magnitude.

The counts underlying the estimate are 1 participant with the endpoint among 21 in the Standard Dosing group and 8 among 24 in the Gestational Age-Based Dosing group. The limited number of events makes the estimate sensitive to individual observations. The displayed proportions and difference should therefore not be treated as highly precise forecasts for another group of patients. No finer detail about the interval calculation or model is reported in the registry record.

A confidence interval is not the range of outcomes for individual participants, and it is not a guarantee that the true effect falls within its endpoints. It quantifies sampling uncertainty under the assumptions of the analysis used. It does not automatically incorporate uncertainty from unreported design details, possible outcome classification issues, missing data, or other sources of bias. The registry does not report enough methodological detail to assess those components.

The unadjusted p value of 0.017 addresses evidence against a null risk difference under the comparison's statistical assumptions; it does not make the effect estimate precise. A small p value and a wide interval can occur together when the estimated direction is relatively clear but the magnitude remains uncertain. For this result, the interval is essential context for the p value and for any interpretation of the size of the group difference.

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 derived from the observed effect, not the trial's original design calculation. For these binary outcomes, the figures are participants per arm. They are not total event counts. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the model assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are planning concepts: power is a property of a proposed design for a specified effect and assumptions, not a probability that the trial's conclusion is correct.

The rows describing 100%, 75%, and 50% of the observed effect use progressively smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same planning assumptions. The illustrated requirements also depend on the particular endpoint and observed effect used in the calculation. They should not be read as a recommendation or as proof that the trial was designed around those values. The original sample-size assumptions are not reported in the registry record.

These figures are not observed power. They are forward-looking illustrations based on the observed effect, and the observed effect itself is uncertain. In particular, planning directly from an estimated effect in a limited trial can yield unstable projections. The sample-size illustrations do not change the interpretation of the trial's posted confidence intervals or establish that the trial had adequate precision for every outcome.

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 = 0.048; treatment proportion p₁ = 0.333; average p̄ = 0.190.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5553 = 1.0884.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5173 = 0.4353.
4. n = (1.0884 + 0.4353)² / (0.2857)² = 28.4, rounded up to 29 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 <- 0.0476190476190476                          # control proportion
p1 <- 0.333333333333333                          # 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(4635839)
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 = 29 (80% power), 38 (90% power)
 75% of observed effect: n per arm = 44 (80% power), 58 (90% power)
 50% of observed effect: n per arm = 80 (80% power), 106 (90% power)
power.prop.test: 28.4 
Simulated power at n = 29 per arm: 0.845 (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

Multiplicity arises when a study evaluates several outcomes or performs several statistical comparisons. Even if each comparison is considered separately, examining many results increases the opportunity for some findings to look notable because of random variation. An adjustment or a clearly defined testing hierarchy can address this issue, but the registry record does not report a multiplicity strategy for the primary and secondary outcomes. The posted secondary comparisons are unadjusted, so their p values should not be treated as though they account for the full set of outcomes.

The registry lists one primary endpoint and multiple secondary outcomes, including thrombosis, anesthesia, delivery, blood loss, transfusion, and anti-factor Xa measures. It does not give a complete statistical analysis plan, specify which secondary analyses were confirmatory or exploratory, or report an adjustment for multiple testing. The record lists zero reported analyses in its analysis field. That means no analyses are listed there; it does not establish that investigators performed no analyses outside the posted record.

Missing-data handling is not reported in the registry record. The posted denominators vary by outcome, and the record does not explain why participants were not included in a particular outcome denominator or how any missing observations were treated. There is no reported description of imputation, sensitivity analyses, or reasons for missingness. Consequently, it is not possible to assess whether the posted comparisons are based on all randomized participants or a subset defined by outcome availability.

The analysis population is also not reported. The record does not say whether participants were analyzed according to randomized assignment, treatment received, or another population definition. Randomization is part of the design, but it does not by itself establish how the results were analyzed. The registry also does not describe protocol deviations, adherence, crossover, or treatment discontinuation beyond the primary measurement timeframe.

These omissions matter because multiplicity, missing outcomes, and analysis population can affect both uncertainty and the interpretation of a treatment comparison. They do not invalidate the descriptive counts, but they limit how fully the posted estimates can be evaluated. The primary comparison is therefore most appropriately read as the result recorded for the reported outcome denominators, with no assumptions added about unreported statistical 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 0% reporting threshold.

The registry reports zero serious adverse events and zero other adverse events in the Standard Dosing group, with 21 participants listed at risk. It reports zero serious adverse events and zero other adverse events in the Gestational Age-Based Dosing group, with 24 participants listed at risk. Deaths are reported as zero in both groups. No serious adverse event terms are listed.

These figures describe the safety events recorded in the registry for the groups and risk denominators shown. They do not establish that either dosing strategy has no risk. When no events are observed in a trial, the results still leave uncertainty about events that could occur in a larger population or over a different period of observation. The record does not provide detailed definitions, event ascertainment procedures, or a separate safety analysis.

The absence of reported events should therefore be read as a descriptive finding, not as proof of equivalent safety or evidence that uncommon harms are excluded. Safety conclusions also depend on the scope and completeness of event collection, which are not described in detail in the registry record.

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

The primary finding is a difference in the proportion of participants whose activated partial thromboplastin time exceeded the specified normal-range threshold. The observed count was higher in the gestational age-based group, and the reported risk difference and confidence interval describe the size and uncertainty of that contrast. This is the result the registry reports; it is not a direct estimate of the effect of dosing on every clinical outcome considered by the study.

The laboratory measure is described as a surrogate marker for eligibility for neuraxial anesthesia. A surrogate can be relevant to a clinical decision without being equivalent to the decision or its consequences. The primary result therefore does not, on its own, establish how often participants received neuraxial anesthesia, whether any delay occurred, or whether pregnancy outcomes differed. Those questions require their own outcome data and interpretation.

The secondary results available in the registry are limited and point in different directions across outcomes. The record does not report numerical findings for several listed measures, and it does not provide a multiplicity plan or complete analysis methods. The reported absence of adverse events is also not proof that no harms can occur. Each of these considerations constrains the strength of any broader inference.

Randomized allocation makes the comparison of assigned groups informative, but it does not remove uncertainty from limited event counts, unreported analysis choices, missing-data handling, or the lack of masking. The registry record also does not give enough detail about participant characteristics, dosing implementation, or outcome assessment to determine how closely the observed results would apply in other settings.

Accordingly, the findings should be described narrowly: the posted primary data show a higher observed frequency of the laboratory threshold outcome in the gestational age-based group, with an unadjusted comparison and a confidence interval that leaves uncertainty about the magnitude. They do not establish a complete clinical effect, a causal explanation for anesthesia decisions, or a definitive safety profile.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its primary outcome sits between a treatment strategy and a clinical decision. The investigators used a laboratory threshold described as a surrogate for neuraxial anesthesia eligibility. That design raises an important interpretation question: even if a dosing strategy changes the surrogate, does the change correspond to a meaningful difference in actual anesthesia eligibility or practice? The registry's primary comparison answers the laboratory question, not the full clinical question.

The results also illustrate why counts, effect estimates, and uncertainty should be read together. The observed counts give the direct record of events; the risk difference communicates the absolute separation between groups; and the confidence interval shows that the estimated magnitude remains uncertain. A p value alone cannot convey that range or explain the outcome's clinical role.

The secondary outcomes make the issue more complex. They include events and processes that matter clinically, but their reported pattern is not uniform and the record does not post numerical results for every listed measure. Unadjusted secondary comparisons across multiple outcomes can be exploratory signals, but they need cautious interpretation. A statistical plan describing prespecification, multiplicity, and analysis populations would help clarify their evidential weight.

Finally, the registry's limited reporting of missing-data handling, analysis methods, and participant disposition constrains reproducibility and appraisal. Reporting these details allows readers to distinguish a result driven by the randomized comparison from one affected by data availability or analysis choices. The trial therefore offers a useful example of how statistical interpretation depends not only on an effect estimate, but also on endpoint meaning, precision, and transparent methods.

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 leaves several trial-specific limitations unresolved. It does not report the dose amounts for either group, the precise dosing schedule, adherence, treatment changes, or the criteria used to determine when heparin was stopped. These details would help readers understand the contrast actually implemented and the timing of outcome measurements.

Although the study is described as randomized and unmasked, the record does not explain sequence generation, allocation concealment, who knew group assignment, or whether outcome assessment was masked. It also does not report baseline characteristics or eligibility criteria. Randomization is valuable, but without these details readers cannot examine group comparability or assess the potential for outcome assessment to be influenced by knowledge of dosing.

The enrollment field lists 46, whereas the primary endpoint reports outcome denominators of 21 and 24. The registry record does not explain the relationship between the enrollment figure and those denominators, or provide a participant flow account. The outcome-specific denominators are clear, but the reasons for the difference in reporting are not. Missing-data handling and the analysis population are also not reported.

The primary outcome is a thresholded surrogate, and the registry does not provide individual laboratory values or report how the threshold related to actual anesthesia decisions. The record does not identify the statistical test or interval method, describe an adjustment strategy for multiple outcomes, or provide the original sample-size justification. The planning illustrations use observed effects and should not be confused with the trial's original design assumptions.

Finally, several listed secondary outcomes do not have numerical results in the registry record. The reported safety counts do not include detailed event definitions or ascertainment procedures. These reporting gaps limit assessment of the trial's methods, the robustness of its secondary findings, and the applicability of the results beyond the participants represented by the posted data.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Heparin Prophylaxis Dosing for Antepartum Hospitalizations (HEPDOSE) — NCT04635839.
• Registry record last updated 2023-04-28; status last verified 2023-04.
• Results first posted 2023-04-28.
• 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

HEPDOSE is a completed, phase 4 randomized parallel-group trial comparing standard unfractionated heparin dosing with gestational age-based dosing for thromboprophylaxis during antepartum hospitalization. The registry describes no masking and lists enrollment as 46. Its primary endpoint is the number of participants with activated partial thromboplastin time above the normal range, measured after heparin dosing through discontinuation.

The posted primary counts are 1 of 21 in the Standard Dosing group and 8 of 24 in the Gestational Age-Based Dosing group. The risk difference is 0.286, with a 95% confidence interval from 0.076 to 0.495 and an unadjusted p value of 0.017. The endpoint is a surrogate for anesthesia eligibility, not a direct clinical outcome. Secondary results are limited, and the registry does not report key details about multiplicity, missing data, analysis populations, or the original sample-size assumptions. The findings should be interpreted with attention to endpoint meaning and uncertainty.