Clinical Study Evaluating the Performance of HEMOBLAST Bellows Compared to FLOSEAL Hemostatic Matrix in Cardiothoracic Operations: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study Evaluating the Performance of HEMOBLAST Bellows Compared to FLOSEAL Hemostatic Matrix in Cardiothoracic Operations (NCT03725098), a randomized na study. The primary outcome is 3 Minute Hemostasis - Hemostatic Success (Yes/no) at 3 Minutes.

2. Clinical Question

The question is about an intraoperative, binary outcome: each participant is classified according to whether hemostasis was achieved within the specified time. It is not a comparison of the amount of bleeding, the time to hemostasis as a continuous measure, or later clinical outcomes. The registry also lists hemostatic success at 5 minutes as a secondary outcome, which provides a later intraoperative assessment but does not replace the primary question.

The posted primary counts are 34 of 53 participants in the HEMOBLAST Bellows arm and 5 of 52 in the FLOSEAL arm. These counts describe the recorded outcome in the two randomized groups. They do not, by themselves, describe how the trial handled missing endpoint observations, deviations from assigned treatment, or other analysis-population decisions; those details are not reported in the registry record.

3. Trial Design

The registry identifies this as a prospective, randomized, controlled, multicenter, post-market clinical study. It compared HEMOBLAST Bellows with FLOSEAL in cardiothoracic operations. The trial is listed as completed, with enrollment of 105. Its start date is 2019-03-01, and its primary completion date is 2019-06-28.

Allocation is recorded as randomized, the model as parallel, and masking as single. The registry does not identify who was masked, so the masking label alone does not establish whether participants, surgeons, outcome assessors, or another group were unaware of treatment assignment. The record lists the phase as NA. It names Biom'Up France SAS as the sponsor.

The two arms received different hemostatic devices: HEMOBLAST Bellows and FLOSEAL. The arm descriptions state that bleeding sites would be treated with the assigned device according to its approved Indications for Use. The registry does not report further details about the operative procedures, site-level treatment decisions, training, or consistency of application across centers.

The primary outcome was hemostatic success within 3 minutes, recorded as a participant count and assessed intraoperatively. The secondary outcome was hemostatic success within 5 minutes, also recorded as a participant count and assessed intraoperatively. The registry record does not report a formal analysis population, the handling of missing data, the original target sample size, or the trial's original sample-size justification. It also does not report a detailed statistical analysis plan or interim-analysis procedures.

The results should therefore be read as a registry record of a randomized comparison and its posted outcome counts, not as a complete account of every design and analysis decision. Randomization supports a comparison between assigned groups, but interpreting the estimates still depends on information about outcome ascertainment, missingness, analysis choices, and protocol conduct that is not reported in the registry record.

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: One additional subject was enrolled due to a delay in the reporting function of the electronic database used for the study. This additional subject is not anticipated to affect the analyses or ethical conduct of the study, as all subjects were treated on-label for an approved device in this post-market study

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 3 Minute Hemostasis - Hemostatic Success (Yes/no) at 3 Minutes, measured over Intraoperative.

The primary endpoint is hemostatic success within 3 minutes, measured intraoperatively and expressed as a count of participants meeting the yes/no criterion. The registry describes the primary objective as testing the superiority of HEMOBLAST Bellows relative to FLOSEAL for the proportion of participants reaching hemostasis within that interval.

A binary endpoint turns each participant's result into one of two categories: success or not success by the stated time. This makes the outcome directly interpretable as the frequency of meeting a clinically defined procedural milestone. It does not retain detail about exactly when hemostasis occurred within the interval, how much bleeding occurred, or what happened after the intraoperative assessment.

In general, a short, prespecified time threshold can make a procedural comparison focused and straightforward to summarize. The chosen threshold also matters: conclusions concern success within 3 minutes, rather than hemostasis at any time or a broader measure of surgical outcome. The registry does not report further endpoint-adjudication details, including how borderline assessments were resolved, whether assessors were masked to treatment, or how missing endpoint observations were classified.

The posted primary outcome counts are 34 of 53 in the HEMOBLAST Bellows group and 5 of 52 in the FLOSEAL group. These are participant counts, not numbers of bleeding sites or separate applications. The registry record does not report a more detailed definition of the participant-level endpoint or whether participants could have multiple treated sites.

7. Results Posted in the Registry

• FLOSEAL (Hemostatic Device): 9.6% (5/52) versus 64.2% (34/53) on control; risk difference -54.5 percentage points (95% CI -69.7 to -39.3), risk ratio 0.15 (0.06–0.35); unadjusted two-proportion z-test p = <0.001.

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.

5 Minute Hemostasis - Hemostatic Success (Yes/no) at 5 Minutes

• 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:
  • FLOSEAL (Hemostatic Device): 44.2% (23/52) versus 92.5% (49/53) on control; risk difference -48.2 percentage points (95% CI -63.5 to -33.0), risk ratio 0.48 (0.35–0.66); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for FLOSEAL (Hemostatic Device) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint: hemostatic success at 5 minutes. The overall direction of its posted comparison is consistent with the primary endpoint, with the observed participant counts favoring HEMOBLAST Bellows. This offers contextual support that the direction was not confined to the primary time threshold, but it does not independently reproduce the primary finding.

The two outcomes are related intraoperative assessments from the same randomized study. They concern the same broad event and are measured at different time thresholds, so they should not be treated as independent pieces of evidence. A pattern that aligns across related outcomes can be informative, but it does not remove uncertainty about outcome assessment, analysis choices, or study conduct.

Unadjusted secondary results generally carry less weight than a prespecified primary result because testing multiple outcomes can increase the chance of at least one apparently notable finding. In general, multiplicity procedures address that issue by adjusting interpretation or the threshold for evidence across a set of tests. The registry record does not report whether such a procedure was planned or applied. Accordingly, the secondary outcome is best used as supportive context rather than as a separate confirmatory claim.

The record lists no reported analyses for the secondary outcome beyond the posted summary comparison. It does not describe whether secondary outcomes were prespecified in a statistical analysis plan, how missing values were handled, or whether any subgroup or sensitivity analyses were undertaken. Those details are not reported in the registry record. The secondary result can therefore inform the overall pattern, but its inferential status and robustness cannot be fully evaluated from the registry entry alone.

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

• 5 Minute Hemostasis - Hemostatic Success (Yes/no) at 5 Minutes

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either meets the hemostasis criterion within 3 minutes or does not. The record gives the number meeting the criterion in each arm and the number of participants in each arm. For this kind of outcome, an analysis can compare proportions, or equivalently compare risks of the recorded success event. The posted comparison uses a risk difference, defined generally as one group's proportion minus the other's. The displayed contrast is FLOSEAL relative to HEMOBLAST Bellows, so a negative direction corresponds to a lower recorded success proportion for FLOSEAL.

What does a risk difference describe?

In general, a risk difference expresses an absolute contrast between two event proportions on the same scale. It answers how far apart the observed proportions are, rather than describing their relative size. The direction depends on which group is subtracted from which. Here the comparison is explicitly oriented with FLOSEAL relative to HEMOBLAST Bellows. This is why direction should be checked before interpreting the sign of an estimate. The posted group counts make the direction understandable without relying on a label alone.

The primary comparison also has a confidence interval. In general, a confidence interval represents a range of values compatible with the data and the method's assumptions, and it conveys uncertainty in the estimated contrast. It is not a guarantee that the true effect lies within that particular interval. The posted interval for the risk difference lies entirely below zero. This is compatible with a lower success proportion in the FLOSEAL group under the stated comparison orientation. Its width also matters: a range may exclude zero while still allowing appreciable uncertainty about the size of the contrast.

What does the p-value add?

The unadjusted primary p-value is reported as p < 0.001. In general, a p-value describes how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it is not the probability that chance alone caused the results. It does not measure the effect's importance or tell how likely the result is to recur. The word “unadjusted” indicates that this reported value is not presented as corrected for multiple testing.

The registry record does not identify a named statistical test, the full set of model assumptions, or whether the primary p-value came from a sponsor analysis or another analysis. The comparison estimates and intervals are simple unadjusted recalculations from the posted group summaries. No discrepancy is flagged between the posted data and these recalculations. They should therefore be interpreted as unadjusted summaries rather than as a substitute for an unreported prespecified analysis plan.

Why does the binary outcome matter?

In general, a binary endpoint is easy to communicate because it states how many participants met a defined criterion. However, it compresses information. It does not show how close a participant who did not meet the time threshold came to it, nor does it distinguish an event just inside the threshold from one occurring earlier. Results may also depend on how the criterion is assessed and how missing or indeterminate observations are treated. Those procedures are not reported in the registry record.

The primary endpoint is framed as superiority. In general, a superiority analysis evaluates whether one treatment has a greater outcome measure than the comparator, rather than whether the treatments are sufficiently similar or whether one meets a noninferiority margin. The registry record does not report a noninferiority margin or an equivalence objective, and the posted primary question is not described in those terms.

Why can over-dispersion matter?

Over-dispersion is a general concern for outcomes whose variation is greater than a statistical model expects. It is especially relevant when modeling counts or clustered observations. The primary endpoint is a participant-level binary count, not a reported continuous or time-to-event outcome. The record does not report a model that assumes a particular dispersion structure, nor does it provide site-level outcome data or a cluster-adjusted analysis. Because this is a multicenter study, potential similarities among participants treated at the same center could matter to inference in some analyses; whether and how the registry analysis accounted for center is not reported. No numerical adjustment for clustering can be inferred from the posted summaries.

General statistical interpretation also depends on how randomization was implemented and preserved, whether outcome assessment was independent of treatment knowledge, and whether the analysis followed assigned groups. The registry identifies randomized allocation and single masking but does not describe sequence generation, concealment, masked roles, protocol deviations, or the analysis population. Those missing details limit independent assessment of the assumptions behind the comparison.

11. Confidence Intervals and Precision

The primary comparison is accompanied by a confidence interval for the risk difference. The interval's two endpoints are both below zero, so the reported range does not include no difference under this comparison's orientation. In practical terms, the posted interval is consistent with a lower proportion of recorded 3-minute successes in the FLOSEAL arm than in the HEMOBLAST Bellows arm.

Precision is not the same as statistical significance. An interval can exclude zero and still span a range of possible effect sizes. In general, a narrower interval indicates more precise estimation, while a wider interval indicates greater uncertainty about the magnitude. The posted primary interval is bounded away from zero but still has a meaningful span. The registry data therefore support a directional contrast more clearly than they establish one exact magnitude.

The group counts are 34 of 53 for HEMOBLAST Bellows and 5 of 52 for FLOSEAL. The inferential summary is unadjusted, and the registry record does not report an adjusted analysis accounting for study center or other covariates. It also does not provide details about missing observations or the endpoint analysis population. Such choices can affect both the estimate and its precision, especially if outcome availability differs by group or center.

For the secondary 5-minute endpoint, the interval for the unadjusted risk-difference comparison also lies below zero. That consistency in direction adds context, but the secondary endpoint should not be treated as a separate confirmation without knowing the testing plan and multiplicity handling. The registry does not report an adjustment for multiple outcomes.

Confidence intervals describe uncertainty under the method used; they do not incorporate every source of uncertainty. They do not account automatically for limitations in endpoint measurement, incomplete reporting, departures from the planned design, or differences between the enrolled participants and other populations. The absence of a detailed statistical plan in the registry record means that the posted interval is best read as an unadjusted precision summary, not a complete characterization of all possible uncertainty.

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. Each figure is the number of participants per arm, not a combined total. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 12 participants per arm for 80% power and 15 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 22 and 29 participants per arm. At 50% of the observed effect, they are 52 and 69 participants per arm. These are hypothetical planning values under the listed assumptions, not enrollment targets reported for this trial.

In general, power is the chance that a specified analysis will detect an effect of the size assumed, if that effect is present and the statistical assumptions hold. The 80% power column and 90% power column therefore represent different planning thresholds: the latter aims for a greater chance of detecting the assumed effect and, under these calculations, requires more participants per arm. Smaller target effects also require more participants, because they are harder to distinguish from sampling variation.

The curve should be interpreted as a visual representation of how the planning requirement changes with the assumed effect size, not as additional observed trial evidence. These figures are not observed power. Observed power is not a useful replacement for reading the effect estimate and its confidence interval; the planning illustrations answer a different question about hypothetical future study sizes.

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 = 0.642; treatment proportion p₁ = 0.096; average p̄ = 0.369.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6823 = 1.3374.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5629 = 0.4738.
4. n = (1.3374 + 0.4738)² / (-0.5454)² = 11.0, rounded up to 12 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 <- 0.641509433962264                          # control proportion
p1 <- 0.0961538461538462                          # 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(3725098)
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 = 12 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 22 (80% power), 29 (90% power)
 50% of observed effect: n per arm = 52 (80% power), 69 (90% power)
power.prop.test: 11 
Simulated power at n = 12 per arm: 0.862 (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 endpoint and one secondary endpoint, each assessed as hemostatic success at a stated intraoperative time. It reports an unadjusted p-value for each comparison but does not report a multiplicity strategy. When multiple hypotheses are tested, the chance of obtaining at least one small p-value can rise. In general, a prespecified testing hierarchy or adjustment can control how results are interpreted across outcomes. Whether either approach was used is not reported in the registry record.

This matters most for the secondary result. The primary endpoint is the stated superiority question, while the secondary endpoint provides additional context. Without a reported plan for controlling multiplicity, the secondary p-value should not be read as if it had the same confirmatory status as a single, prespecified primary test. The registry does not report whether other outcomes were assessed but not posted, so the complete family of tests cannot be established from the record.

Missing-data handling is also not reported. The posted group denominators are 53 for HEMOBLAST Bellows and 52 for FLOSEAL for the primary and secondary outcomes, but the registry does not describe whether these represent all randomized participants, all treated participants, or participants with available outcome data. It does not state how missing, indeterminate, or unevaluable assessments were handled. The outcome population field is empty, and the analysis population cannot be determined from that field.

The registry record also does not report an intention-to-treat analysis, a per-protocol analysis, sensitivity analyses for missing data, or rules for protocol deviations. These are not claims that such analyses were absent from the full study; they are details not reported in the registry record. Without them, readers cannot assess whether the posted comparison follows randomized assignment for all participants or relies on a subset defined after randomization.

Finally, the study is identified as multicenter, but the record does not report whether analyses accounted for center. Nor does it report interim analyses, a detailed statistical analysis plan, or the original sample-size rationale. These omissions constrain interpretation of the inferential results and prevent a full assessment of how the posted comparisons relate to the study's prespecified analysis strategy.

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 safety counts report zero participants affected by serious adverse events in the HEMOBLAST Bellows group and zero in the FLOSEAL group. The counts for participants affected by other adverse events are also zero in both groups, and deaths are recorded as zero in both groups. These are the posted safety figures for the risk groups identified in the registry.

Zero recorded events should be read as a description of the registry entries, not as proof that no event occurred in any participant or that the devices have no safety risks. The record does not provide event narratives, detailed definitions, severity criteria beyond the serious-event category, exposure duration, or the completeness and length of safety follow-up. It also does not explain how adverse events were collected or adjudicated.

Safety comparisons with no recorded events in either group cannot characterize the relative frequency of uncommon events from these counts alone. The registry figures are limited to the listed categories and do not replace a broader safety assessment. No advice about treatment choice follows from these entries.

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

The registry results describe a randomized comparison of two hemostatic devices during cardiothoracic operations. More participants in the HEMOBLAST Bellows arm met the primary 3-minute success criterion in the posted counts than in the FLOSEAL arm. The unadjusted comparison has p < 0.001, and the confidence interval for the risk difference lies entirely below zero when expressed as FLOSEAL relative to HEMOBLAST Bellows. Together, these summaries indicate a clear directional difference in the recorded primary outcome within this trial.

The result does not establish that the observed contrast will be identical in other settings, procedures, centers, or patient groups. The registry does not report detailed eligibility criteria, center-level results, endpoint adjudication procedures, analysis populations, or the handling of missing outcome data. Each can affect how confidently a trial result can be carried beyond the posted comparison.

The endpoint is limited to hemostatic success by the 3-minute threshold. It does not, on its own, describe longer-term outcomes, complications, recovery, resource use, or other measures of surgical performance. The secondary 5-minute assessment is related to the primary outcome and cannot be treated as independent confirmation. Nor do the posted safety counts establish the absence of safety risks.

A p-value below a conventional threshold does not prove a treatment effect, measure its clinical importance, or give the probability that the result occurred by chance. The effect estimate and its interval provide information about direction and precision, but the registry entry does not report all details needed to evaluate the original analysis plan. The estimates are unadjusted summaries and should be interpreted within those limits.

These results therefore describe what was recorded in this completed post-market randomized study. They do not supply medical advice or determine which device should be used for an individual operation. Their meaning depends on the trial's population, how the endpoint was measured, and analysis details that are not reported in the registry record.

17. Why This Trial Matters Statistically

This study illustrates why the form of an endpoint matters. The primary outcome is a binary participant-level milestone: hemostasis achieved within 3 minutes or not. That makes the result accessible as counts in each randomized group, while also discarding information about the exact time to success and the amount or course of bleeding.

The comparison also shows the value of stating which group is the reference. The reported risk difference is oriented as FLOSEAL relative to HEMOBLAST Bellows, so its negative direction corresponds to fewer observed successes in the comparator group. A statistical estimate is easier to interpret when its scale and orientation are kept clear alongside the arm-specific counts.

Precision and evidence against no difference are related but distinct. The unadjusted p-value is below 0.001, while the confidence interval provides a range of plausible contrasts under the analysis method. Reading both helps avoid reducing a result to a threshold alone. The posted interval excludes zero, but the registry record does not report the detailed analysis plan, missing-data approach, or whether center was accounted for.

The secondary endpoint provides a useful check on whether the observed direction is similar at another time threshold, but the outcomes are related and multiplicity handling is not reported. This is a practical reminder that agreement across related endpoints can add context without constituting an independent trial or a separately confirmed primary result.

Finally, planning illustrations based on an observed effect should not be confused with the study's original design justification. Their values depend on stated hypothetical assumptions and illustrate how required sample size changes with the target effect and desired power. The original design assumptions are not reported, so the illustrations cannot explain why the completed trial enrolled its recorded number of participants.

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 details unclear. Although the study is labeled randomized and single-masked, it does not describe the randomization sequence, allocation concealment, or who was masked. It also does not provide enough detail to assess how consistently the devices were applied across centers or how the intraoperative endpoint was determined.

The primary endpoint is a yes/no assessment at a short time threshold. The record does not define the adjudication process, identify the assessor, or explain how uncertain or missing assessments were handled. The posted arm denominators are available, but the registry does not state whether they represent every randomized participant or a subset with available outcomes. The analysis population and missing-data procedures are not reported.

The registry provides no detailed statistical analysis plan, original sample-size justification, interim-analysis information, or report of whether center was incorporated into the analysis. It also does not report multiplicity handling for the secondary endpoint. The unadjusted comparisons therefore cannot be fully checked against a prespecified testing strategy from the registry record alone.

The safety information is limited to aggregate counts of participants affected by serious adverse events, other adverse events, and deaths. Event definitions, exposure time, follow-up completeness, and individual event details are not reported. Zero counts in the posted record cannot resolve those reporting limitations.

Finally, the endpoint concerns intraoperative hemostasis, and the registry record does not report broader clinical outcomes in the information summarized. The findings should be interpreted as applying to the recorded procedural outcome in this study rather than as a complete evaluation of all potential benefits and harms.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Study Evaluating the Performance of HEMOBLAST Bellows Compared to FLOSEAL Hemostatic Matrix in Cardiothoracic Operations — NCT03725098.
• Registry record last updated 2020-01-13; status last verified 2020-01.
• Results first posted 2020-01-13.
• 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 record describes a completed, prospective, randomized, controlled, multicenter, post-market, parallel-group study comparing HEMOBLAST Bellows with FLOSEAL in cardiothoracic operations. Enrollment is 105. The study is listed as single-masked; the identity of the masked party is not reported.

The primary outcome was hemostatic success within 3 minutes. The posted counts are 34 of 53 for HEMOBLAST Bellows and 5 of 52 for FLOSEAL, with an unadjusted p-value of p < 0.001. The secondary outcome was hemostatic success within 5 minutes, and its observed direction is consistent with the primary result.

The record lists zero participants affected by serious adverse events, other adverse events, or deaths in either arm. It does not report the original sample-size justification, detailed analysis plan, multiplicity handling, analysis population, or missing-data procedures. Accordingly, the posted results support interpretation of the recorded outcomes but leave important design and analysis details unresolved.