Study of Fampridine-SR Tablets in Multiple Sclerosis Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Fampridine-SR Tablets in Multiple Sclerosis Patients (NCT00483652), a randomized phase 3 study. The primary outcome is Responders Based Upon the Timed 25-Foot Walk [T25FW].

2. Clinical Question

The registry describes the study’s purpose as testing whether people treated with Fampridine-SR were significantly more likely to show consistent walking improvement than people treated with placebo. The endpoint definition required a participant to show faster walking speed at least three visits out of a possible four during the double-blind period, compared with the maximum value achieved in five non-double-blind, no-treatment visits. Those reference visits occurred four times before the double-blind period and once after it.

This is a question about meeting a specific repeated-measure response rule, not simply about a single walking test or average walking speed. The comparison therefore depends on both the visit-based definition and the reference value used for each participant. The posted result reports the number of responders in each randomized group and an unadjusted comparison of those counts. It does not, by itself, describe every aspect of walking ability or establish how the result relates to outcomes beyond those recorded in the registry.

3. Trial Design

This was a randomized, quadruple-masked, parallel-group Phase 3 study comparing Fampridine-SR with placebo in participants with multiple sclerosis. The registry lists Acorda Therapeutics as the sponsor and records the study as completed. The study began in 2007-05, with primary completion in 2008-02. Recorded enrollment was 240.

The intervention was Fampridine-SR 10 mg b.i.d., meaning twice daily; the comparator was placebo. A parallel-group design assigns participants to one group for the comparison rather than having every participant receive both study treatments. Random allocation is intended, in general, to make treatment groups comparable at the point of assignment, while masking is intended to limit influences on participant care, outcome assessment, or reporting. The registry identifies quadruple masking but does not specify in the record which roles were masked.

The primary outcome was assessed in the Modified Intention-to-Treat [ITT] population. The posted endpoint counts include 119 participants in the Fampridine-SR group and 118 in the placebo group. The registry does not report why these endpoint denominators differ from recorded enrollment, or provide further details about participant flow in the record.

Assessments were listed for Days -21, -14, -7, 0, 14, 28, 42, 56, 63, and 77. The primary responder definition refers to four possible visits during the double-blind period and five non-double-blind no-treatment visits. The registry record does not give the original protocol’s sample-size justification, the trial’s full statistical analysis plan, or further operational details about the visit schedule. Those omissions limit how fully the design and analysis decisions can be reconstructed from the registry record alone.

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: Two weeks of single-blind placebo run-in to establish baseline walking speeds

Double-blind Treatment Period

Reasons for not completing this period:

Post-study Follow-up

Analysis population for the primary outcome, as defined in the registry: Modified Intention-to-Treat \[ITT\] population

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 Responders Based Upon the Timed 25-Foot Walk [T25FW], measured over Days -21, -14, -7, 0, 14, 28, 42, 56, 63, 77.

The primary endpoint is the number of participants who qualified as responders based on the Timed 25-Foot Walk [T25FW]. A responder had to show faster walking speed at least three out of a possible four visits during the double-blind period than the maximum value achieved across five non-double-blind no-treatment visits. The primary outcome is recorded for the Modified Intention-to-Treat [ITT] population.

This rule turns repeated walking assessments into a binary outcome: each participant either meets the response definition or does not. In general, a repeated-visit rule can reflect consistency across assessments rather than relying on a single measurement. The comparator is a participant-specific reference based on the highest value during the specified no-treatment visits, so the endpoint is tied to both performance during treatment and that reference period.

The registry lists assessment days as Days -21, -14, -7, 0, 14, 28, 42, 56, 63, and 77. It does not report further detail about how missing or unusable visit measurements affected responder classification. The endpoint therefore gives a defined, study-specific measure of walking response, but its interpretation should remain tied to that definition rather than generalized to every aspect of mobility or daily function.

7. Results Posted in the Registry

• Fampridine-SR 10 mg b.i.d. Treatment: 42.9% (51/119) versus 9.3% (11/118) on control; risk difference 33.5 percentage points (95% CI 23.2 to 43.9), risk ratio 4.60 (2.52–8.37); 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.

Change in Lower Extremity Manual Muscle Test [LEMMT]

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Fampridine-SR 10 mg b.i.d. Treatment: mean 0.09 versus 0.04 on control; difference 0.05 (95% CI -0.01 to 0.11), standardized effect d = 0.21; z-test p = 0.104.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fampridine-SR 10 mg b.i.d. Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists change in Lower Extremity Manual Muscle Test [LEMMT] as a secondary outcome and posts a result for that measure. The primary endpoint and this secondary endpoint address different aspects of the study: the primary outcome classifies repeated walking performance using a responder rule, whereas LEMMT records change on a muscle-test scale. Their results need not move in lockstep, and agreement or disagreement between them would not by itself establish the validity of either measure.

The secondary comparison is less decisive statistically than the primary result: its uncertainty includes no mean difference. This offers a more cautious evidential pattern across the outcomes that have posted results. It does not negate the primary finding, but it does mean the secondary result does not supply equally clear corroboration. The registry lists two outcome measures overall and has one secondary outcome result posted; the record therefore offers a limited basis for judging consistency across secondary outcomes.

In general, secondary outcomes can help describe whether a primary result is accompanied by changes in related measures or other aspects of the study. They are often interpreted with greater caution when many outcomes or tests may have been considered. Testing multiple outcomes increases the chance of finding a statistically notable result by chance if no adjustment or hierarchy is applied. The registry record does not report a multiplicity adjustment, testing hierarchy, or complete analysis plan. The secondary result is unadjusted, so it should be treated as contextual evidence rather than as a separate confirmatory finding.

The record also does not give enough information to determine whether all planned secondary analyses were completed, whether additional outcomes were measured but not posted, or how the outcome was handled in the full analysis. Those limitations argue for describing the available pattern without treating it as a comprehensive assessment of secondary evidence.

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

• Change in Lower Extremity Manual Muscle Test [LEMMT]

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: participants are classified as responders or non-responders according to the T25FW rule. The comparison uses the number classified as responders in each group and the number counted in that group. For a binary outcome, the group-specific proportion is the number with the event divided by the group denominator. The registry’s posted comparison expresses the contrast as a risk difference and also includes relative measures.

What does the risk difference describe?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the other. It is an absolute measure, so it describes the size of the gap on the original proportion scale. Here, the posted risk difference is 0.335. The direction is defined by the treatment-versus-placebo comparison in the registry result: a positive value corresponds to a larger responder proportion in the Fampridine-SR group. The measure remains specific to the responder definition and the participants included in the comparison.

How do relative measures differ?

A risk ratio compares the two event proportions by division. An odds ratio compares the odds of the event in one group with the odds in the other. Both are relative measures and can be useful for expressing contrasts, but they are not interchangeable with an absolute difference. The registry posts a risk ratio and an odds ratio alongside the risk difference. Their confidence intervals communicate uncertainty on their respective scales. The counts and absolute measure help ground these relative values in the observed data.

What does a p-value tell the reader?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be, if that null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The posted primary p-value is unadjusted and reported as <0.001. Since the registry record does not describe the trial’s full analysis plan, this value should not be interpreted as accounting for all possible design or analysis choices.

Why are confidence intervals useful?

In general, a confidence interval gives a range of estimates compatible with the observed data under a specified method and its assumptions. It conveys both the direction and the precision of an estimate. A narrow interval indicates more precision than a wide interval, while an interval that includes a null value indicates that the data are compatible with that value under the interval method. A confidence interval does not capture every source of uncertainty, including possible bias, outcome misclassification, or limitations in the study design.

The primary interval is for the risk difference. The secondary outcome is continuous and is reported as a mean change, so its comparison uses a mean difference and a different interpretation. In general, a mean difference compares group averages, while the standard deviation describes variation among observations within a group. The registry reports group means and standard deviations for LEMMT and posts an unadjusted mean-difference comparison. The registry does not report a model or analysis details for that secondary comparison.

What can be said about the analysis population?

The primary endpoint is identified as applying to the Modified Intention-to-Treat [ITT] population. In general, an intention-to-treat approach seeks to retain participants in the groups to which they were assigned, but the precise meaning of a modified population depends on the study’s definition. The registry record does not provide further criteria for this population or describe how missing outcome information was handled. The posted denominators are therefore important when interpreting the counts, and should not be assumed to represent every randomized participant.

The registry records randomized allocation and quadruple masking, but the information summarized in the record does not give the allocation procedure, the roles masked, or the details of any stratification. The full statistical analysis plan, including model specifications and prespecified tests, is not reported in the registry record. No interim analyses or stopping rules are reported in the registry record; their absence from the record does not establish what the protocol may have specified.

Why do the planning illustrations differ from the observed trial?

The planning illustrations are based on observed effects and stated assumptions, rather than on a reconstruction of the original trial design. In general, a sample-size calculation estimates the number of participants needed to detect an effect under chosen assumptions about the effect size, variability or event rate, significance level, allocation, and analysis method. Changing those assumptions changes the estimate. The registry does not report the trial’s original sample-size justification or design assumptions, so the illustrations should not be read as the trial’s prospective plan.

The posted primary comparison is a straightforward unadjusted summary comparison. A more complete trial analysis could include methods specified in the protocol, but those details are not reported in the registry record. This distinction matters: a simple calculation from summary data can help readers understand the observed contrast, but it cannot establish which analysis was prespecified or whether any additional analyses were conducted outside the registry entries.

11. Confidence Intervals and Precision

The primary risk difference is 0.335, with a 95% confidence interval from 0.232 to 0.439. The interval lies above zero, indicating that the compatible values under this unadjusted calculation favor a higher responder proportion in the Fampridine-SR group. Its limits also show that the estimate is not exact: the data are compatible with a range of absolute differences, not only the point estimate.

In general, a confidence interval describes uncertainty from sampling under the method used. It is not a guarantee about the true value, and it does not account automatically for biases, outcome-definition choices, missing data, or unreported analysis decisions. The posted interval is based on the unadjusted group comparison and should be understood in that scope. The registry record does not report a sponsor analysis interval or enough analysis detail to establish whether a different prespecified method was used.

The relative measures also have intervals: the risk ratio is 4.597, with a 95% confidence interval from 2.524 to 8.375; the odds ratio is 7.295, with a 95% confidence interval from 3.555 to 14.97. These intervals are on different scales and should not be compared directly with the risk-difference interval. The absolute difference and the underlying group counts provide an accessible view of the observed separation.

For LEMMT, the posted mean difference is 0.05, with a 95% confidence interval from -0.010 to 0.110. This interval includes zero, so the secondary estimate is compatible with no mean difference as well as with values on either side of zero under the unadjusted method. In general, an interval’s width reflects precision, while its location reflects the values most compatible with the data. Neither interval resolves the registry record’s unanswered questions about missing data, multiplicity, or the original analysis plan.

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 illustrations are participant counts per arm, not total event counts. The outcomes in this record are a binary responder outcome and a continuous measure, so the displayed quantities are participants per arm. In general, these calculations estimate a sample size under specified assumptions; they are planning illustrations based on the observed effect, not a report of the trial’s original design.

The stated assumptions 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 at the stated fraction of the observed effect. The registry does not report the original sample-size justification or the trial’s own design assumptions, so the illustrations cannot be used to infer those decisions.

The 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if the assumed effect and analysis conditions hold. The 90% power column gives the corresponding estimate for a design with a 90% chance under the same stated assumptions. These are design probabilities under hypothetical conditions, not probabilities that the study result is true. These figures are not observed power.

Rows using a smaller fraction of the observed effect require more participants per arm in the illustrations. In general, smaller differences are harder to distinguish from random variation, so a larger sample is needed to achieve the same target power, all else held constant. The numbers should be read as sensitivity to the assumed effect size, not as evidence that the original trial was designed around any one row or that its observed result has a particular probability of replication.

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 = 0.093; treatment proportion p₁ = 0.429; average p̄ = 0.261.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6210 = 1.2172.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5740 = 0.4831.
4. n = (1.2172 + 0.4831)² / (0.3354)² = 25.7, rounded up to 26 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 <- 0.0932203389830508                          # control proportion
p1 <- 0.428571428571429                          # 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(483652)
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 = 26 (80% power), 34 (90% power)
 75% of observed effect: n per arm = 42 (80% power), 55 (90% power)
 50% of observed effect: n per arm = 81 (80% power), 107 (90% power)
power.prop.test: 25.7 
Simulated power at n = 26 per arm: 0.835 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, contrast, time point, subgroup, or statistical test. In general, conducting multiple tests can increase the chance that at least one result appears statistically notable by chance. Researchers can address this through prespecified outcome hierarchies or statistical adjustments, but such choices must be documented to interpret the results appropriately. The registry record does not report a multiplicity strategy or explain how the primary and secondary outcomes were prioritized in the analysis.

The registry identifies the T25FW responder measure as primary and lists change in LEMMT as a secondary outcome. One secondary result is posted, and the record lists two outcome measures overall. The registry’s analysis entries are empty. It is therefore not possible from the registry record to establish which statistical tests were prespecified, whether any adjustment was used, or whether analyses not represented in the registry were conducted. The posted p-values are unadjusted and should not be assumed to control the overall false-positive risk across outcomes or analyses.

For the primary outcome, the population is described as Modified Intention-to-Treat [ITT]. The registry does not give the operational definition of that population or report how participants with missing assessments were treated. Because responder classification depends on repeated visits, missing or unusable measurements could affect whether a participant meets the response rule. The record does not state whether missing visits were imputed, whether participants were excluded, or what sensitivity analyses were performed.

Random allocation is reported, but the registry record does not explain the allocation sequence or concealment procedures. Quadruple masking is listed, but the identities of the masked roles are not specified in the information summarized for this study. The original statistical analysis plan, covariate adjustments, interim analyses, and stopping rules are not reported in the registry record. These gaps do not show that a particular procedure was absent; they mean the registry entry does not allow readers to verify it.

These uncertainties do not erase the posted counts or their unadjusted comparison. They do limit how confidently the registry results can be interpreted as a full account of the planned and completed analysis. The clearest reading separates what is recorded—the endpoint definition, group counts, and posted summaries—from decisions that remain undocumented in the registry record.

15. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroesophageal reflux disease (0.8%), chest discomfort (0.8%), urinary tract infection (0.8%), complex partial seizure (0.8%), pyelonephritis (0.8%).

The registry reports serious adverse events for 5 of 120 participants at risk in the Fampridine-SR group and 3 of 119 at risk in the placebo group. These are counts of participants affected, as recorded in the adverse-event summary. The registry also lists other adverse events for 103 of 120 participants in the Fampridine-SR group and 79 of 119 in the placebo group. These categories should be read separately; the record does not explain whether the same participant could contribute to more than one event term.

The serious adverse-event terms listed include Gastroesophageal Reflux Disease, Chest discomfort, Urinary tract Infection, Complex partial seizure, Pyelonephritis, and Cholelithiasis, each recorded as 0.8%. The listed percentages describe the registry’s reported terms and should not be treated as a full account of event severity, timing, or causality. The registry record does not report deaths in the information summarized for this study.

In general, adverse-event counts describe events observed and recorded during the study; they do not by themselves establish that a study treatment caused an event. The groups’ counts also do not replace a complete safety analysis, which would require further context such as event definitions, duration of exposure, and analysis methods. Those details are not reported in the registry record.

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

The posted primary result indicates that a larger proportion of participants in the Fampridine-SR group met the study’s T25FW responder definition than in the placebo group. The unadjusted risk difference and its confidence interval describe the size and precision of that observed contrast. The finding is specific to a rule requiring faster walking speed at least three of four possible double-blind visits compared with the maximum value from five non-double-blind no-treatment visits.

That result does not mean every participant in the Fampridine-SR group met the responder definition, nor does it describe the experience of every person with multiple sclerosis. It is based on the participants counted in the Modified Intention-to-Treat [ITT] population and the registry’s stated outcome definition. The registry does not report enough information to determine how missing visit data were managed or why the endpoint denominators differ from recorded enrollment.

The result also does not establish an effect on every aspect of walking, muscle strength, daily activity, or quality of life. The posted secondary outcome is a different measure and provides less decisive evidence. No broader claims about outcomes that are not reported in the registry record can be drawn from these results.

Statistical evidence and clinical interpretation are related but distinct. In general, a small p-value describes compatibility with a null model under particular assumptions; it does not state how important an outcome is to participants or how benefits and harms should be weighed. The registry’s unadjusted primary comparison is statistically clear as a comparison of the posted responder counts, but it cannot answer questions that depend on the study’s full analysis plan, multiplicity handling, or unreported clinical context.

The record supports a bounded conclusion: the observed groups differed on this defined walking-responder outcome, with uncertainty quantified by the posted interval. It does not, on its own, settle the interpretation of the full trial or supply medical advice. The original design assumptions, detailed analysis methods, and missing-data procedures are not reported in the registry record, so those aspects should remain open rather than being inferred.

17. Why This Trial Matters Statistically

This study illustrates why outcome definitions matter in clinical-trial interpretation. The primary endpoint is not simply a single walking-time measurement: it classifies participants using repeated visits and a participant-specific reference from no-treatment visits. The resulting binary responder comparison is understandable as a count, but it necessarily compresses a pattern of repeated measurements into a yes-or-no category. Readers need the definition to understand what the event represents.

It also illustrates the value of reporting absolute and relative comparisons together. The risk difference expresses the observed separation on an absolute scale, while the risk ratio and odds ratio express it on relative scales. These measures can emphasize different aspects of the same data. Keeping the group counts and endpoint definition in view helps prevent a relative estimate from being interpreted without its underlying context.

Precision and statistical evidence are not identical to completeness of reporting. The primary confidence interval is clearly separated from zero, but the registry record does not include the full statistical analysis plan, missing-data approach, or multiplicity strategy. Those omissions matter because they affect how a reader can assess the analysis choices, not because they change the posted counts themselves.

The secondary result provides another statistical lesson: related outcomes can show different patterns because they measure different constructs and use different scales. A less conclusive secondary result neither cancels the primary finding nor independently confirms it. Where multiplicity handling is not reported, secondary findings deserve careful, contextual interpretation.

Finally, planning calculations based on an observed effect are not a substitute for the original sample-size rationale. They illustrate how assumptions about effect size and power relate to participant requirements, while leaving the trial’s actual design decisions undocumented. Separating these types of evidence helps readers distinguish observed results, statistical uncertainty, and information that the registry does not report.

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 offers limited detail for reconstructing the trial’s analysis. It identifies the primary population as Modified Intention-to-Treat [ITT] but does not define the population further, describe participant flow, or explain the relationship between recorded enrollment and the endpoint denominators. It also does not report how missing T25FW visits affected classification under the repeated-visit responder rule.

The primary comparison available in the record is unadjusted. The registry lists no analysis entries and does not report the sponsor’s full model, any covariate adjustment, or sensitivity analyses. The original sample-size justification and the trial’s own planning assumptions are also not reported in the registry record. Consequently, the planning illustrations based on observed effects cannot be taken as documentation of the original design.

The registry lists quadruple masking but does not specify the masked roles in the information summarized for this study. It does not report allocation concealment details, the multiplicity strategy, interim analyses, or stopping rules. These are reporting gaps, not proof that the study lacked such procedures.

Only one secondary result is posted, and the record does not establish whether all planned secondary analyses are represented. The posted secondary comparison is unadjusted, and no correction for multiple outcomes is reported. The serious adverse-event summary provides group counts and selected terms, but the record does not provide details about event timing, exposure, causality assessment, or the complete safety analysis. These limitations narrow what can be concluded from the registry entry and make it important to keep interpretation tied to the outcomes and summaries it actually records.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Fampridine-SR Tablets in Multiple Sclerosis Patients — NCT00483652.
• Registry record last updated 2016-02-04; status last verified 2016-01.
• Results first posted 2011-04-14.
• 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

NCT00483652 is a completed, randomized, quadruple-masked, parallel-group Phase 3 study of Fampridine-SR 10 mg b.i.d. compared with placebo in participants with multiple sclerosis. Recorded enrollment was 240. The primary outcome was the number of participants meeting a T25FW walking-responder definition in the Modified Intention-to-Treat [ITT] population.

The posted primary counts were 51 of 119 in the Fampridine-SR group and 11 of 118 in the placebo group. The unadjusted risk difference was 0.335, with a 95% confidence interval from 0.232 to 0.439 and p < 0.001. One secondary outcome result, change in LEMMT, is posted. The registry record does not report the full statistical analysis plan, original sample-size justification, multiplicity strategy, or missing-data procedures.