A Study on the Use of Tanakan® for Recovery of Neurological Impairment Following Ischaemic Stroke: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study on the Use of Tanakan® for Recovery of Neurological Impairment Following Ischaemic Stroke (NCT00276380), a randomized phase 3 study. The primary outcome is Percentage of Subjects With Modified Rankin Score of Less Than 3 at the End of Study Period..

2. Clinical Question

3. Trial Design

The registry describes a Phase III, multicentre, randomized, double-blinded, parallel-group, placebo-controlled clinical study. It lists Ipsen as sponsor and the study status as completed. The study began in 2003-02, with primary completion in 2009-03. Enrollment was 204. The primary outcome report gives 102 participants in each treatment group.

Participants were assigned to EGb761® or placebo, with acetylsalicylic acid described in both arm regimens. The active treatment was EGb761® 240 mg/day for 6 months, administered orally alongside acetylsalicylic acid 325 mg/day. The placebo arm also received placebo for 6 months alongside acetylsalicylic acid 325 mg/day. The registry labels the design parallel group and the masking double-blind; further details about who was masked or how masking was maintained are not reported in the registry record.

The primary outcome was assessed at Day 168. The record describes the modified Rankin scale assessment at baseline and at Day 28, Day 84, and Day 168. The primary analysis was conducted in the Intention-To-Treat population, defined as participants with at least one treatment dose. This definition identifies the analysis population, but the registry record does not describe how participants with missing Day 168 outcome data were handled.

The registry lists seven outcome measures in total and six secondary outcomes. These include modified Rankin outcomes at earlier visits, and changes in SCAG, Barthel Index, Mini Mental State, and NIHSS subscores. It records 12 analyses, but the detailed analysis plan, prespecified hierarchy among outcomes, and any adjustment for multiple testing 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: The inclusion (baseline) visit on Day 0 was to take place within 3-8 days following an ischaemic stroke.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: This analysis was performed on the Intention-To-Treat (ITT) population which includes all subjects having at least one treatment dose.

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 Percentage of Subjects With Modified Rankin Score of Less Than 3 at the End of Study Period., measured over Day 168.

The primary endpoint was the percentage of participants with a modified Rankin score below 3 at Day 168. The modified Rankin scale is used to describe disability and dependence in daily activities after stroke. The registry describes it as a six-point scale, with scores from 0, meaning no symptoms at all, through 5, meaning severe disability. Scores of 1 and 2 represent no significant disability and slight disability; scores of 3, 4, and 5 represent moderate, moderately severe, and severe disability.

Using a threshold turns the scale into a binary outcome for the primary comparison: each participant is counted on one side of the threshold or the other. The endpoint therefore describes the proportion meeting the specified score criterion, rather than the average score or the distribution across all scale points. This can make the result straightforward to interpret as a group proportion, but it does not show how scores differ within either side of the threshold. A participant just below the threshold and one with a much lower score both contribute to the same category.

The endpoint was recorded at Day 168, the end of the stated study period. The registry also lists modified Rankin assessments at baseline, Day 28, and Day 84, but those earlier assessments are not the primary endpoint described in the results. The record identifies the primary analysis population as the Intention-To-Treat population, including participants who received at least one treatment dose.

7. Results Posted in the Registry

• EGb761®: 59.8% (61/102) versus 64.7% (66/102) on control; risk difference -4.9 percentage points (95% CI -18.2 to 8.4), risk ratio 0.92 (0.75–1.14); unadjusted two-proportion z-test p = 0.470.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because participants are classified according to whether their modified Rankin score at Day 168 was below 3. A binary outcome can be summarized as a count and a proportion in each group. The registry reports percentages of 59.8 for EGb761® and 64.7 for placebo, and the posted result includes the corresponding event counts of 61 and 66. These group summaries retain whether a participant met the threshold, but not the exact score within either category.

What does the risk difference express?

The unadjusted risk difference compares the proportion meeting the threshold in the EGb761® group with the proportion in the placebo group. The posted estimate is -0.049, with a confidence interval from -0.182 to 0.084. Under this direction of subtraction, a negative value means the observed proportion was lower in the EGb761® group. The interval includes zero, the value corresponding to no difference in proportions, and extends to either side of zero. This means the estimate is uncertain about both the direction and the magnitude of the group contrast.

General statistical interpretation: a risk difference is expressed on the probability scale, so its size can be read as an absolute contrast in proportions. It is distinct from a relative measure such as a risk ratio or odds ratio. Different measures answer related but not identical questions, and their numerical values should not be compared as if they were on the same scale.

What does the confidence interval add?

A confidence interval describes uncertainty around an estimated effect, under the statistical method and assumptions used to construct it. It is not a guarantee that the true value lies within the displayed range, and it does not state the probability that the null hypothesis is true. In this case, the risk-difference interval includes the no-difference value and also includes values in both directions. Its width indicates that the estimated group contrast is not precise enough to isolate a narrow range of possible effects.

The registry also gives recalculated relative measures: the risk ratio is 0.924, with an interval from 0.746 to 1.145, and the odds ratio is 0.811, with an interval from 0.460 to 1.431. These are unadjusted recalculations from the posted summaries. Their intervals also include the null value for the corresponding relative measure. They express the data on different scales from the risk difference, and none of these estimates should be interpreted without their intervals.

How should the p-value be read?

The recalculated unadjusted p-value is 0.47. General statistical interpretation: a p-value evaluates how unusual the observed result, or a result more extreme, would be if a specified null hypothesis and the analysis assumptions held. It does not measure the probability that the treatment effect is zero, and it does not measure the probability that the finding occurred by chance. The p-value does not indicate the size or clinical importance of a difference; the effect estimate and its interval are needed for that context.

The sponsor’s reported result is a Cochran-Mantel-Haenszel analysis of an odds ratio: 0.83, with a 95% confidence interval from 0.46 to 1.48 and p = 0.52. General statistical interpretation: the Cochran-Mantel-Haenszel approach can combine information across strata. The strata and the precise implementation are not reported in the registry record, so the basis for any adjustment cannot be described further. This sponsor analysis is not numerically identical to the simple unadjusted recalculation because it reports an odds ratio and uses a different analysis method.

What does the analysis population mean?

The registry defines the primary Intention-To-Treat population as including participants who had at least one treatment dose. This definition gives a boundary for who was included in the stated analysis population. It does not, by itself, establish that all randomized participants contributed a Day 168 outcome, or explain the handling of missing scores. The method for missing outcome data is not reported in the registry record. General statistical interpretation: missing outcome handling can affect estimates if the observed participants differ systematically from those without measured outcomes, so the analysis population definition and missing-data method both matter.

Why do other outcomes matter to interpretation?

The registry lists six secondary outcomes, including other modified Rankin summaries and changes in SCAG, Barthel Index, Mini Mental State, and NIHSS subscores. It records 12 analyses. When multiple outcomes or analyses are examined, the chance of obtaining an apparently notable result somewhere among them can increase if each is interpreted without accounting for multiplicity. General statistical interpretation: multiplicity procedures can control or describe this issue, but the procedure used for these analyses is not reported in the registry record. The number of listed outcomes alone does not show whether such a procedure was planned or applied.

10. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is -0.049, with a confidence interval from -0.182 to 0.084. The interval spans zero, so the posted data are compatible with no difference as well as with differences in either direction under this analysis. The range is broad relative to the point estimate, which limits how precisely the size and direction of the contrast can be characterized.

The arm percentages are 59.8 for EGb761® and 64.7 for placebo. These are descriptive estimates from the trial groups, not exact values for all possible participants in the broader population. The interval around the recalculated risk difference reflects sampling uncertainty under the calculation’s assumptions. It does not account for every possible source of uncertainty, such as limitations in outcome measurement, missing data, or choices in analysis.

The posted relative-effect intervals likewise include their null values: the risk ratio is 0.924, with an interval from 0.746 to 1.145, and the recalculated odds ratio is 0.811, with an interval from 0.460 to 1.431. The sponsor-reported odds ratio is 0.83, with a 95% confidence interval from 0.46 to 1.48. The sponsor and recalculated odds ratios are not exactly the same because their analyses differ. Each interval should be interpreted on the scale of its own measure.

General statistical interpretation: greater precision would mean a narrower interval around the estimate, while a wider interval leaves more uncertainty about plausible effect sizes. The interval does not establish that all values within it are equally plausible, nor does it identify which value is true. Here, the range of compatible values makes it inappropriate to treat the point estimate alone as a precise description of the treatment contrast.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for this binary outcome, rather than total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The original design assumptions used for the trial are not reported in the registry record.

The 80% power column gives the participants per arm indicated by the planning calculation to have an 80% chance of detecting the assumed effect under those assumptions. The 90% power column gives the corresponding planning count for a 90% chance. These are design-planning quantities: they describe the sample size associated with a chosen assumed effect and test procedure, rather than a property of the completed trial’s result.

For planning for 100% of the observed effect, the figures are 1,534 participants per arm for 80% power and 2,053 participants per arm for 90% power. For planning for 75% of the observed effect, they are 2,710 participants per arm for 80% power and 3,628 participants per arm for 90% power. For planning for 50% of the observed effect, they are 6,057 participants per arm for 80% power and 8,108 participants per arm for 90% power. Smaller assumed effects require more participants because a smaller contrast is harder to distinguish from sampling variation under the stated calculation assumptions.

These figures are not observed power. Observed power is not a useful substitute for examining the estimated effect and its confidence interval; the planning figures instead show how sample-size requirements change when the assumed effect and target power change. The trial’s own sample-size justification is not reported in the registry record.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.647; treatment proportion p₁ = 0.598; average p̄ = 0.623.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6855 = 1.3436.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6847 = 0.5762.
4. n = (1.3436 + 0.5762)² / (-0.0490)² = 1,533.9, rounded up to 1,534 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 <- 0.647058823529412                          # control proportion
p1 <- 0.598039215686274                          # 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(276380)
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 = 1,534 (80% power), 2,053 (90% power)
 75% of observed effect: n per arm = 2,710 (80% power), 3,628 (90% power)
 50% of observed effect: n per arm = 6,057 (80% power), 8,108 (90% power)
power.prop.test: 1533.9 
Simulated power at n = 1,534 per arm: 0.801 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor’s reported analysis is a Cochran-Mantel-Haenszel odds ratio of 0.83, with a 95% confidence interval from 0.46 to 1.48 and p = 0.52. The recalculation from the posted group summaries is unadjusted and reports a risk difference of -0.049, with a confidence interval from -0.182 to 0.084 and p = 0.47. The recalculated unadjusted odds ratio is 0.811, with a confidence interval from 0.460 to 1.431.

These estimates need not match exactly. The sponsor’s analysis uses a Cochran-Mantel-Haenszel method, while the recalculations are simple, unadjusted comparisons from the posted summaries. The sponsor reports an odds ratio, and the primary recalculation reports an absolute risk difference. The registry record does not describe the sponsor analysis’s strata or other implementation details. The record flags no discrepancy between its reported and recalculated results. The posted analyses all indicate substantial uncertainty, and their confidence intervals include the respective null values.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists seven outcome measures, of which six are secondary, and records 12 analyses. The primary result concerns the modified Rankin threshold at Day 168. Secondary outcomes include modified Rankin results at Day 28 and Day 84, the distribution across scale points at several assessments, and mean changes from baseline in SCAG, Barthel Index, Mini Mental State, and NIHSS subscores. The outcomes cover related but distinct aspects of disability, function, cognition, and neurological status.

When researchers evaluate multiple outcomes, time points, or analyses, interpreting each result as if it were the sole test can overstate the evidence from the collection of results. General statistical interpretation: multiplicity approaches may adjust significance thresholds, define a hierarchy, or otherwise account for the number and relationship of tests. Whether any such approach was used, and how the analyses were prioritized, is not reported in the registry record. The count of listed outcomes and analyses does not establish that all were primary or that an adjustment was omitted.

The record defines the primary analysis population as the Intention-To-Treat population with at least one treatment dose. It does not report the number of participants with missing Day 168 scores, the reasons for missing outcome data, or the method used to handle missingness. It also does not report whether the reported analysis included every participant in that defined population. These details matter because an analysis of available outcomes can be affected if missingness is related to treatment assignment or outcome.

The record does not report the original sample-size justification, any interim analyses, or the detailed statistical analysis plan. It also does not provide enough information to establish whether the reported method was prespecified or whether analyses were changed during the study. These absences limit assessment of the full analysis process, but they do not change the numerical results reported for the primary endpoint.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ischaemic stroke (2.0%), cerebral haemorrhage (1.0%), transient ischaemic attack (1.0%), sick sinus syndrome (1.0%), circulatory collapse (1.0%).

The registry’s serious adverse event summary lists 12 serious adverse events among 101 participants at risk in the EGb761® group and 7 among 100 at risk in the placebo group. It also lists other adverse events for 16 among 101 at risk in the EGb761® group and 17 among 100 at risk in the placebo group. The record lists 5 deaths in the EGb761® group and 3 in the placebo group.

The serious adverse event terms listed with percentages are ischaemic stroke at 2.0%, cerebral haemorrhage at 1.0%, transient ischaemic attack at 1.0%, sick sinus syndrome at 1.0%, circulatory collapse at 1.0%, and vertigo at 1.0%. These are the terms and percentages recorded; the summary does not provide further information about timing, severity details, individual participant overlap, or causality.

These counts should be read as safety summaries, not as proof that a treatment caused or prevented an event. The denominators differ between the displayed groups, and the registry summary does not explain the relationship between the event counts and the number of participants who experienced at least one event. It also does not report a comparative statistical analysis for these safety results. The figures describe what the record lists, while leaving uncertainty about attribution and comparative risk.

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

The primary endpoint compares the proportion of participants who had a modified Rankin score below 3 at Day 168. The posted percentages were 59.8 for EGb761® and 64.7 for placebo. The unadjusted risk-difference estimate was -0.049, with a confidence interval from -0.182 to 0.084. The interval includes zero and values in both directions, so the observed point estimate should not be treated as a precise estimate of the direction or size of a group difference.

The endpoint gives a useful summary of whether participants crossed a specified disability threshold, but it does not show the full distribution of scores. It cannot indicate, by itself, whether the groups differed among participants below the threshold or among participants at or above it. Nor does the primary result establish what happened on the listed secondary outcomes. The record includes measures of function, cognition, and neurological status, but the results for those outcomes are not reported in the registry record.

The comparison concerns EGb761® added to acetylsalicylic acid, against placebo alongside acetylsalicylic acid. It is therefore not a comparison of EGb761® with no background treatment. The study’s randomized, double-blinded, parallel-group design describes its planned comparison, but the result still depends on the endpoint definition, analysis population, handling of missing data, and analysis method. Missing-data procedures and several details of the analysis plan are not reported in the registry record.

General statistical interpretation: a result with a confidence interval that includes the null value does not prove that there is no effect. It means that the estimate is uncertain enough that the data, under the analysis assumptions, are compatible with a range that includes no difference. The p-values of 0.47 for the unadjusted recalculation and 0.52 for the sponsor’s analysis are not probabilities that a treatment works or does not work. They should be considered alongside the estimates, intervals, and limits of the available record.

The findings therefore support a bounded reading: the registry reports the observed group proportions and analyses, but the primary estimate is imprecise. It does not warrant a claim that one regimen is superior or equivalent, and it does not settle the effects on outcomes beyond the endpoint reported.

17. Why This Trial Matters Statistically

This trial illustrates why an observed difference and the precision of that difference need to be read together. The group percentages are not identical, and the unadjusted risk-difference estimate is -0.049. Yet its confidence interval, from -0.182 to 0.084, covers zero and values on either side. Focusing only on the estimate would leave out substantial uncertainty; focusing only on whether a p-value crosses a threshold would also omit the range of effects compatible with the data.

It also shows how the choice of measure shapes interpretation. A risk difference describes an absolute contrast in proportions, whereas a risk ratio and odds ratio describe relative contrasts. The sponsor’s reported analysis uses a Cochran-Mantel-Haenszel odds ratio, while the posted recalculations include an unadjusted risk difference and relative measures. These are connected descriptions of the same binary endpoint, but they are not interchangeable. Their methods and scales need to be identified before results are compared.

The primary outcome is a dichotomized modified Rankin measure. Such a threshold can provide a clear summary, but it compresses the scale and does not reveal the full score distribution. The registry’s additional outcome measures point to other dimensions of recovery, while the number of listed analyses makes it important to understand how outcomes were prioritized and how multiplicity was addressed. That information is not reported in the registry record.

Finally, the study gives a practical example of the distinction between a trial result and a planning illustration. The sample-size figures are based on observed effects and stated assumptions; they are not the study’s original design justification and are not observed power. This distinction helps keep a retrospective planning calculation from being mistaken for evidence about the certainty of the completed trial’s result.

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

The registry record does not report the detailed eligibility criteria or baseline characteristics needed to judge how closely the enrolled population represents particular clinical settings. It gives the study’s enrollment and primary analysis group sizes, but those numbers alone do not describe the participants’ starting levels of disability or other prognostic features. Baseline assessment of the modified Rankin scale is described, but baseline group results are not included in the primary result summary.

The primary endpoint is a thresholded score at Day 168. The result does not show the complete modified Rankin distribution at that visit, and the primary comparison cannot describe changes within categories. The record lists earlier assessments and additional measures, but the outcome results for those measures are not reported in the registry record.

The registry does not report the method for missing Day 168 outcome data, the number of participants missing that assessment, or the reasons for any missingness. The Intention-To-Treat definition includes those who received at least one treatment dose, but the record does not explain how that population was represented in the endpoint analysis. The detailed sponsor-analysis strata and the full statistical analysis plan are also not reported.

The record lists multiple outcomes and analyses, but does not state whether or how multiplicity was handled. It does not report the trial’s original sample-size justification or interim analyses. These gaps limit evaluation of design and analysis decisions beyond the results displayed in the registry. The safety summary also does not give event-level details, participant overlap, timing, or causal attribution. These limitations call for careful interpretation of the reported estimates rather than a claim that the result answers every question about recovery or safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study on the Use of Tanakan® for Recovery of Neurological Impairment Following Ischaemic Stroke — NCT00276380.
• Registry record last updated 2019-01-08; status last verified 2019-01.
• Results first posted 2018-02-19.
• 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

This completed Phase III study evaluated EGb761® (Tanakan®) alongside acetylsalicylic acid after ischaemic stroke, compared with placebo alongside acetylsalicylic acid. The registry describes a multicentre, randomized, double-blinded, parallel-group, placebo-controlled design, enrollment of 204, and primary completion in 2009-03.

The primary endpoint was the percentage of participants with a modified Rankin score below 3 at Day 168. The reported percentages were 59.8 for EGb761® and 64.7 for placebo. The unadjusted recalculated risk difference was -0.049, with a confidence interval from -0.182 to 0.084 and p = 0.47. The sponsor reported an odds ratio of 0.83, with a 95% confidence interval from 0.46 to 1.48 and p = 0.52. Both analyses leave substantial uncertainty about the primary contrast. The registry record does not report several details needed to assess missing data, multiplicity, or the original sample-size rationale.