TASALL - TachoSil® Against Liquor Leak: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TASALL - TachoSil® Against Liquor Leak (NCT01355627), a randomized phase 3 study. The primary outcome is Percentage of Participants With Clinically Evident Verified Post-Operative Cerebrospinal Fluid Leak or Clinically Evident Pseudomeningocele or Treatment Failure.

2. Clinical Question

This was a randomized, open-label comparison, so assignment was randomized but masking was absent. The central estimand represented by the posted percentages is the proportion with the primary endpoint in each group, rather than time until an event. The analysis therefore addresses whether the observed event proportions differed, not whether the timing or duration of events differed. The registry states a superiority objective. The posted estimates can be read as evidence about the observed group contrast and its precision; they do not, on their own, establish that every component of the composite behaves in the same way or that the treatment effect is the same across clinical settings.

3. Trial Design

TASALL (NCT01355627) was a phase 3, randomized, open-label, controlled, multicentre, parallel-group trial. Its official title describes a comparison of TachoSil® with current practice in dura sealing techniques for prevention of post-operative cerebrospinal fluid leaks in patients undergoing skull base surgery. The registry lists an enrollment of 726 and describes randomization in a 1:1 ratio. The primary endpoint results are reported for 361 participants assigned to TachoSil® and 365 assigned to current practice.

The intervention and comparator are both recorded as procedures. The registry's brief summary identifies TachoSil® as an adjunct in sealing the dura mater and states that efficacy was evaluated post-operatively. The specific range of techniques constituting current practice, and detailed procedural instructions for either group, are not reported in the registry record. Because masking was listed as none, the trial was open label. The registry does not report additional detail about concealment of allocation or blinding of outcome assessment.

The primary endpoint was assessed daily from randomization until discharge and at an efficacy follow-up visit at week 7 ± 1 week. The primary outcome timeframe is described as up to 8 weeks. The registry also reports a secondary endpoint assessed at least once before discharge from the neurosurgical ward, with an expected discharge after an average of 10 days, and a timeframe extending up to 28 weeks. The brief summary describes safety follow-up 28 ± 2 weeks after surgery.

The registry lists a completed status, a start date of 2011-04, and a primary completion date of 2013-06. It reports one posted secondary outcome and two outcome measures. Details of the original sample-size justification, the planned statistical analysis, and any interim analyses are 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: Participants requiring dura sealing techniques for the prevention of post-operative cerebrospinal fluid (CSF) leaks were enrolled; 726 participants were randomized equally in 1 of 2 treatment groups, TachoSil® or Current practice group.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Population included all enrolled randomized patients.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Baseline Measures were based on the Full Analysis Set that included all enrolled randomized patients.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Clinically Evident Verified Post-Operative Cerebrospinal Fluid Leak or Clinically Evident Pseudomeningocele or Treatment Failure, measured over Up to 8 Weeks (7 Weeks ± 1 Week).

The primary endpoint is the percentage of participants with at least one of three events: a clinically evident, verified post-operative cerebrospinal fluid leak; a clinically evident pseudomeningocele; or treatment failure. This is a composite endpoint, meaning that different event types are combined into a single outcome for the primary comparison. The registry defines verification of a cerebrospinal fluid leak through a glucose concentration test and/or a β-2-transferrin test. A pseudomeningocele required a visible or palpable fluctuant fluid accumulation at or adjacent to the surgical incision, with suspicion that the fluid was cerebrospinal fluid. Treatment failure included applying a new or different treatment after the study treatment, or a third application of all or part of the selected study treatment on the outside of the dura.

Using a composite can capture several clinically relevant ways in which the intended sealing outcome may not be achieved. It also means the overall percentage does not reveal which component drove the result. The registry does not provide component-specific primary results in the posted outcome data, so the combined percentage should not be interpreted as a separate estimate for each event type. The endpoint is binary at the participant level: a participant either met the composite definition during the stated assessment period or did not. The efficacy assessment was made daily through discharge and again at the scheduled follow-up at week 7 ± 1 week, within the recorded timeframe of up to 8 weeks.

7. Results Posted in the Registry

• Current Practice Group: 8.2% (30/365) versus 6.9% (25/361) on control; risk difference 1.3 percentage points (95% CI -2.6 to 5.1), risk ratio 1.19 (0.71–1.98); unadjusted two-proportion z-test p = 0.510.

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.

Percentage of Participants With Post-Surgical Non-Clinically Evident Post-Operative Pseudomeningocele

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Current Practice Group: 3.0% (11/365) versus 3.0% (11/361) on control; risk difference -0.0 percentage points (95% CI -2.5 to 2.5), risk ratio 0.99 (0.43–2.25); unadjusted two-proportion z-test p = 0.979.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Current Practice Group and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns non-clinically evident post-operative pseudomeningocele. Its overall pattern is broadly similar between groups, with the reported percentages at 3.0% in each group. The unadjusted comparison is close to zero and its p-value is 0.979. This is consistent with little observed separation in this secondary outcome, while its confidence interval still represents uncertainty about the underlying difference.

This secondary outcome is related to, but distinct from, the primary composite. The primary definition includes clinically evident pseudomeningocele alongside verified cerebrospinal fluid leak and treatment failure; the secondary outcome concerns non-clinically evident pseudomeningocele. The two endpoints therefore capture different aspects of post-operative fluid accumulation and should not be treated as interchangeable. The secondary result does not explain which component contributed to the primary composite, and the posted information does not give a component-by-component breakdown of the primary endpoint.

Secondary outcomes generally carry less confirmatory weight when multiple outcomes or comparisons are examined without a reported adjustment plan. Testing several outcomes increases the chance of apparently notable findings arising by chance. The registry record does not report a multiplicity strategy, endpoint hierarchy, or prespecified confirmatory role for the secondary result. Its estimate is consequently useful as descriptive context, but should not be read as independent confirmation of the primary finding or as a basis for a strong conclusion on its own.

The similarity of the observed secondary percentages and the absence of a clear separation in the primary comparison point to a generally close observed pattern across these posted outcomes. This does not show that the outcomes are identical, nor does it establish that the groups have the same risk in every relevant subgroup or over every period. The secondary endpoint's stated timeframe extends up to 28 weeks, whereas the primary efficacy timeframe is up to 8 weeks, so comparisons should retain the distinction in measurement and follow-up.

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

• Percentage of Participants With Post-Surgical Non-Clinically Evident Post-Operative Pseudomeningocele

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary percentage: each participant either met the composite endpoint during follow-up or did not. For each group, the registry reports the percentage and a 95% confidence interval. A confidence interval gives a range of values compatible with the observed data under the method used to construct it. It reflects sampling uncertainty; it does not capture every possible source of bias, variation in clinical practice, or uncertainty about how the endpoint was assessed.

What does the risk difference express?

The unadjusted risk difference compares the observed event proportions by subtracting the TachoSil® proportion from the current-practice proportion. Positive values therefore indicate a higher observed percentage in current practice; negative values indicate a higher observed percentage in the TachoSil® group. The recalculated estimate is 0.013, and its 95% confidence interval runs from -0.025 to 0.051. The interval crosses zero, the value representing no difference in proportions. This is why the estimate should be read together with its interval rather than as a definitive group ordering.

This is an unadjusted recalculation from the posted summary statistics. It does not account for covariates or other features that may have been included in the sponsor's regression model. The registry labels the sponsor's method as logistic regression and reports an odds ratio. Since the model specification and covariates are not reported in the registry record, the regression estimate cannot be independently reconstructed from the posted results. The unadjusted estimate and the sponsor's model estimate address the group comparison on different scales and may differ without necessarily indicating an error.

Why use an odds ratio?

Logistic regression models the odds of a binary outcome. An odds ratio compares those modeled odds between groups; it is not the same as a difference in percentages. The registry reports an odds ratio of 0.82 and p = 0.485. No confidence interval for that odds ratio is reported in the registry record. Without the model details or a confidence interval, the precision of that estimate cannot be evaluated as fully as the unadjusted risk difference. Its p-value is evidence from the reported regression test, not a measure of effect size or a probability that the null hypothesis is true.

For a rare outcome, odds and risks can be numerically similar, but they remain distinct measures. General statistical interpretation should preserve the measure actually reported rather than translating the odds ratio into an unreported percentage or risk difference. The registry's reported logistic result also has no stated direction of coding beyond the group labels, so the numerical odds ratio should be read with the sponsor's analysis description rather than assigned an unrecorded interpretation.

Why can over-dispersion matter?

General: binary-outcome methods often rely on a model for how outcomes vary across participants. Over-dispersion means the data vary more than the model expects. If it is present but ignored, standard errors and confidence intervals can be too optimistic. The registry record does not report an assessment of over-dispersion or a specific correction, so no claim can be made about whether it affected this analysis. This general issue is relevant when evaluating model-based results, particularly when details of the model are limited.

How should the p-values be read?

The recalculated unadjusted p-value is 0.51, while the registry's logistic-regression p-value is 0.485. Each is associated with its own analysis and assumptions. A p-value describes how unusual data at least as inconsistent with a null hypothesis would be if that hypothesis and the model assumptions held. It is not the probability that the treatments are equivalent, nor does it measure the clinical importance of a difference. A p-value above a conventional threshold does not prove no effect; a p-value below a threshold would not by itself establish clinical importance. The registry does not state its planned significance threshold in the trial's original analysis plan.

Randomization supports a comparison between assigned groups by reducing systematic differences in expectation, but it does not guarantee that all observed differences arise only from the intervention. Open-label assignment can affect care, reporting, or outcome assessment. The outcome definitions include observable and test-confirmed criteria, but the record does not specify assessor masking or an independent adjudication process. These design considerations are separate from the mathematical uncertainty represented by the confidence intervals.

11. Confidence Intervals and Precision

The group-level 95% confidence intervals for the primary percentage are 4.5% to 10.1% for TachoSil® and 5.6% to 11.5% for current practice. These intervals show uncertainty around each group's estimated percentage. They are not ranges containing 95% of individual participants' outcomes, and they do not directly give the confidence interval for the difference between groups.

The more direct comparative measure is the unadjusted risk difference. Its estimate is 0.013, and its 95% confidence interval extends from -0.025 to 0.051. Because that range includes zero, it is compatible with no difference as well as with differences in either direction. Its width also indicates that the data do not pin down the contrast to a narrow range. The posted estimate is therefore more informative when read with its uncertainty interval than when read as a single point value.

Confidence intervals depend on the statistical method and assumptions used to construct them. They represent sampling uncertainty under those assumptions, not protection from limitations such as missing outcome data, measurement differences, or the open-label design. The registry identifies the primary analysis population but does not report a detailed missing-data method, so the intervals cannot resolve uncertainty about how unobserved outcomes were handled.

The sponsor's logistic-regression result has a reported odds ratio and p-value but no confidence interval in the registry record. Its precision is therefore less directly visible in the posted result. The absence of that interval should not be filled by deriving one from unreported model details. Overall, the percentage intervals and the risk-difference interval support a cautious reading: the observed percentages are close, but the comparative estimate is not precise enough to establish that the underlying group difference is exactly zero.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are per arm because the listed outcomes are binary percentages; they are not total-event counts. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. These calculations are planning illustrations based on the observed effect, not the trial's original sample-size justification; that original justification is not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 6,561 participants per arm for 80% power and 8,783 participants per arm for 90% power. Planning for 75% of the observed effect gives 11,435 participants per arm for 80% power and 15,308 participants per arm for 90% power. Planning for 50% of the observed effect gives 25,213 participants per arm for 80% power and 33,752 participants per arm for 90% power. These are hypothetical planning quantities under the stated assumptions, not participants enrolled in this trial.

In plain terms, the 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under the assumptions. The 90% power column applies a higher target chance of detection and consequently lists a larger planning requirement for the same effect assumption. Smaller effects need more participants because they are harder to distinguish from random variation. The displayed curve should be read as a visual representation of the same planning relationship, not as an additional result from the trial. This is not observed power: it does not describe the trial's achieved probability of finding a result after the data were collected.

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 = 0.069; treatment proportion p₁ = 0.082; average p̄ = 0.076.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3741 = 0.7333.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3740 = 0.3148.
4. n = (0.7333 + 0.3148)² / (0.0129)² = 6,560.5, rounded up to 6,561 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 <- 0.0692520775623269                          # control proportion
p1 <- 0.0821917808219178                          # 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(1355627)
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 = 6,561 (80% power), 8,783 (90% power)
 75% of observed effect: n per arm = 11,435 (80% power), 15,308 (90% power)
 50% of observed effect: n per arm = 25,213 (80% power), 33,752 (90% power)
power.prop.test: 6560.5 
Simulated power at n = 6,561 per arm: 0.794 (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. Analyses Reported by the Sponsor

The registry's own reported primary analysis uses logistic regression and gives an odds ratio of 0.82 with p = 0.485. The posted analysis does not include a confidence interval for that odds ratio. The separately recalculated comparison is an unadjusted risk difference of 0.013, with a 95% confidence interval from -0.025 to 0.051 and p = 0.51. These estimates use different effect measures and analysis approaches, so their numerical values should not be compared as though they were the same statistic.

The recalculation uses the posted group summary statistics and does not reproduce a regression model. The registry does not report the covariates, coding details, or other model specifications needed to reconstruct the sponsor's analysis. The registry record does not flag a discrepancy between the analyses. The sponsor's result is therefore best understood as the reported model-based analysis, while the recalculation is a transparent unadjusted summary comparison. Neither p-value alone establishes equivalence or clinical importance, and the missing confidence interval for the sponsor's odds ratio limits direct assessment of its precision.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial used a formal multiplicity adjustment for testing the primary and secondary outcomes, whether an endpoint hierarchy was prespecified, or whether secondary analyses were intended to be confirmatory. These details matter because repeated testing can increase the chance of a nominally unusual result even when there is no underlying difference. Without a documented strategy, secondary p-values should be treated as descriptive or exploratory rather than as definitive evidence.

The primary analysis population is described as the Full Analysis Population, including all enrolled randomized patients. The primary outcome counts and percentages are posted for the two randomized groups. However, the registry does not report detailed rules for inclusion in each analysis, how protocol deviations were handled, or whether any post-randomization exclusions occurred. The posted denominator should therefore be understood as the denominator used for the reported result, not as proof that every randomized participant had complete outcome information.

Missing outcome data and their handling are not reported in the registry record. The record does not describe imputation, a missing-at-random assumption, sensitivity analyses, or procedures for participants who did not complete follow-up. This limits assessment of whether the posted percentages could be affected by incomplete ascertainment. The registry also does not report a detailed statistical analysis plan, covariate adjustment plan, or assumptions behind the logistic-regression model.

Interim analyses and any rules for early stopping are not reported in the registry record. The original sample-size justification and the trial's own design assumptions are also not reported. The planning illustrations based on the observed effect cannot substitute for those design details. These reporting gaps do not invalidate the posted numbers, but they constrain how fully the analysis can be audited and how strongly confirmatory claims can be made. The completed status and posted results identify the recorded outcome information; they do not fill in unreported decisions about multiplicity, missing data, or analysis conduct.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hydrocephalus (2.8%), pneumonia (1.9%), meningitis (1.4%), sepsis (1.4%), cerebral ischaemia (1.1%).

The safety results list serious adverse events for 94 of 362 participants at risk in the TachoSil® group and 97 of 364 participants at risk in the Current Practice Group. Other adverse events are listed for 92 of 362 and 102 of 364 participants at risk, respectively. These are registry-reported counts and denominators; no additional rates or between-group safety effect estimates are calculated. Deaths are not reported in the registry record.

The registry also lists serious adverse event terms and percentages, including hydrocephalus at 2.8%, pneumonia at 1.9%, meningitis at 1.4%, sepsis at 1.4%, cerebral ischaemia at 1.1%, and cerebrospinal fluid leakage at 1.1%. These entries describe reported event terms, not necessarily events judged to be caused by the assigned procedure. The registry does not provide enough detail to assess relatedness, severity grading, timing, or repeated events. The count summaries should therefore be read as descriptive safety reporting, not as proof of a causal difference or a complete comparison of safety profiles.

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

The posted primary results describe the proportion of participants who met a composite definition of clinically evident verified cerebrospinal fluid leak, clinically evident pseudomeningocele, or treatment failure during follow-up of up to 8 weeks. The observed percentages were 6.9% with TachoSil® and 8.2% with current practice. The unadjusted risk-difference interval includes zero and spans differences in either direction. The registry's logistic-regression analysis also reports a p-value that does not indicate clear separation between the groups.

These findings do not establish that the groups are equivalent. A result that does not show a clear difference is not the same as evidence that any true difference is absent; equivalence or non-inferiority requires an appropriate design and prespecified margins, which are not reported in the registry record. Nor do the results establish that TachoSil® works or does not work. They describe the posted estimates and their uncertainty for the outcome as defined in this trial.

The composite endpoint combines distinct events. The overall result does not reveal how many participants experienced each component separately or whether the components had different patterns across groups. The primary outcome also concerns the defined follow-up period and the trial's population of patients elected for skull base surgery. It should not be generalized automatically to other procedures, settings, or patient populations.

The open-label design and limited reporting of assessment procedures are relevant when considering how outcomes were identified and recorded. Randomization is an important design feature for comparative inference, but it does not eliminate uncertainty from sampling, missing data, measurement, or analysis choices. The registry record does not provide the full protocol or statistical analysis plan needed to assess all such issues. A balanced reading is that the observed primary percentages were close, while the comparative estimate remains uncertain and the posted information does not support a definitive conclusion of equality or superiority.

18. Why This Trial Matters Statistically

This trial illustrates why a comparative clinical result should be read through its endpoint definition, effect measure, and uncertainty rather than through a single p-value. The primary outcome is a composite, combining a verified cerebrospinal fluid leak, a clinically evident pseudomeningocele, and treatment failure. That choice creates a single summary outcome for the superiority question, but it also means the overall percentage cannot show which event type accounts for the result. Clear interpretation depends on retaining the full clinical definition.

The reported group percentages are close, and the unadjusted risk-difference confidence interval includes zero while extending in both directions. This makes precision central to interpretation: the data do not identify a narrow range for the underlying contrast. The sponsor's logistic-regression result adds a model-based estimate, but it is reported on the odds-ratio scale and lacks a confidence interval in the registry record. Comparing the two analyses therefore requires attention to their different methods and measures.

The trial also demonstrates the difference between a planning illustration and the original design calculation. The posted illustrations use the observed effect and stated statistical assumptions; they do not reveal the assumptions used when the trial was designed. A very small observed contrast can lead to large illustrative planning requirements, but such calculations do not indicate the probability that this completed trial would have produced a significant result.

Finally, the record makes some design features clear—randomization, parallel groups, and open-label conduct—while leaving important analysis details unreported. Recognizing those limits is part of statistical interpretation, not a reason to disregard the observed data. The trial is informative about what was recorded for its defined population and outcomes, while the strength and scope of conclusions remain bounded by the precision and reporting available.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint combines clinically different events, and the posted primary result does not separate the composite into its components. Consequently, the overall percentage cannot show whether verified leaks, pseudomeningoceles, or treatment failures contributed most to the group comparison. The secondary outcome concerns non-clinically evident pseudomeningocele and does not supply a component-level account of the primary endpoint.

The registry records an open-label design. It does not report whether outcome assessors were masked, whether an independent committee adjudicated events, or whether assessment procedures were standardized across centres beyond the stated definitions and schedule. Some endpoint components involve observable findings or treatment decisions; the available record does not establish how open-label conduct may have influenced their ascertainment.

The description of current practice is broad, and the specific sealing techniques used in the comparator group are not reported in the registry record. This limits understanding of how uniform the comparison was across participating centres and how directly it represents a single alternative technique. Detailed procedural information for the TachoSil® group is also not reported.

The registry does not report a full statistical analysis plan, the original sample-size rationale, interim-analysis procedures, multiplicity handling, missing-data methods, or detailed logistic-regression specifications. The sponsor's odds ratio has no posted confidence interval. These omissions limit independent assessment of model choices, precision, and the robustness of the analysis. The primary estimate and its unadjusted interval remain interpretable as posted summary statistics, but they cannot resolve these unreported design and analysis questions.

Finally, the primary follow-up is up to 8 weeks, while the safety follow-up is described as 28 ± 2 weeks after surgery and the secondary outcome timeframe extends up to 28 weeks. Conclusions about the primary efficacy endpoint therefore concern its stated assessment window, not outcomes beyond that period.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: TASALL - TachoSil® Against Liquor Leak — NCT01355627.
• Registry record last updated 2014-07-25; status last verified 2014-06.
• Results first posted 2014-07-25.
• 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.

23. Record Summary

TASALL (NCT01355627) was a completed phase 3, randomized, open-label, parallel-group trial comparing TachoSil® with current practice as an adjunct in dura sealing during skull base surgery. The registry lists enrollment of 726 and reports primary outcome results for 361 participants in the TachoSil® group and 365 in the Current Practice Group.

The primary outcome was a composite of clinically evident verified cerebrospinal fluid leak, clinically evident pseudomeningocele, or treatment failure, assessed up to 8 weeks. The observed percentages were 6.9% and 8.2%, respectively. The unadjusted risk-difference estimate was 0.013, with a 95% confidence interval from -0.025 to 0.051. The registry's logistic-regression analysis reports an odds ratio of 0.82 and p = 0.485.

The posted secondary outcome concerns non-clinically evident post-operative pseudomeningocele. Safety results are descriptive counts; deaths are not reported in the registry record. Important details—including the original sample-size justification, missing-data procedures, multiplicity strategy, and full model specifications—are not reported in the registry record. Interpretation should therefore focus on the defined outcomes, posted estimates, and their uncertainty.