Safety and Efficacy of AVP-923 in PBA Patients With ALS or MS: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of AVP-923 in PBA Patients With ALS or MS (NCT00573443), a randomized phase 3 study. The primary outcome is PBA Episode Rate Ratio (Post/Pre), Regression Adjusted.

2. Clinical Question

The study’s stated objectives included assessing safety, tolerability, and efficacy of both doses in people with PBA associated with ALS or MS. Pharmacokinetic parameters were also an objective in a subset of the study population. The registry does not report the size or composition of that subset.

This is a comparison of treatment groups, not a test of whether individual participants had any episodes. The outcome is expressed as a rate ratio: each arm’s treatment-period episode rate is considered relative to its baseline rate, then the treatment groups are compared with placebo. The registry reports separate sponsor analyses for each dose against placebo.

3. Trial Design

The registry classifies this as a Phase 3, randomized, parallel-group study with quadruple masking. Its official title describes a double-blind, randomized, placebo-controlled, multicenter design. Enrollment was 326, and the study status is completed. The recorded start was 2007-12 and primary completion was 2009-06.

There were three double-blind groups: AVP-923-30, AVP-923-20, and placebo. The dose regimens began with once-daily dosing for 1 week, followed by twice-daily dosing for 11 weeks. The stated treatment period was 12 weeks. The primary endpoint timeframe is baseline to Day 84.

The primary endpoint description says the analysis included randomized subjects in the double-blind phase and enrolled subjects in the open-label extension phase. The registry also lists a separate open-label AVP-923-30 safety group. Details of how participants entered the extension, how long they were followed there, and whether extension results contributed to the primary efficacy comparisons are not reported in the registry record.

The registry does not report the randomization sequence, allocation concealment procedures, the masking roles, or whether randomization was stratified. It also does not report the original sample-size justification or the trial’s planned power assumptions. The planning illustrations accompanying the posted summary statistics are not evidence about the assumptions used to design the original trial.

The trial studied PBA in participants with ALS or MS, but group-specific counts for those underlying diseases are not reported in the registry record. Consequently, the posted primary results do not establish how the estimates differ between the ALS and MS populations.

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.

Double-Blind Phase

Reasons for not completing this period:

Open-Label Extension Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) population - included all randomized subjects for the double-blind phase and all enrolled subjects for the open-label extension phase.

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 PBA Episode Rate Ratio (Post/Pre), Regression Adjusted, measured over Baseline to Day 84.

The primary endpoint was the ratio of the episode rate during the 84-day treatment period to the episode rate during baseline. Participants recorded episodes each day in a diary. A value below 1 means the estimated episode rate during treatment was lower than the baseline rate; the endpoint is a ratio, not a count of episodes or a difference in the number of episodes.

The sponsor’s endpoint model adjusted for study site and underlying disease and used longitudinal negative binomial regression. This type of model is used for repeated count data, such as daily episode counts. As a general statistical point, count data can vary more than a simple Poisson model assumes; negative binomial regression can accommodate this over-dispersion by allowing additional variation. The registry does not report model diagnostics or the amount of over-dispersion in these data.

Using a treatment-to-baseline rate ratio allows the analysis to express change relative to each participant’s baseline rate while comparing groups over the treatment period. The registry reports adjusted arm estimates and sponsor comparisons against placebo. These are distinct summaries: an arm’s ratio describes its treatment-period rate relative to baseline, while the sponsor’s comparative analysis estimates the relationship between groups’ episode-rate reductions.

The daily diary is the recorded source for the episode count. The registry does not report how missing diary days were handled, how baseline rates were calculated when diary records were incomplete, or whether additional endpoint definitions were tested. Those details matter because incomplete or inconsistent recording can affect estimates of repeated event rates.

7. Results Posted in the Registry

• AVP-923-30: mean 0.25 versus 0.47 on control; difference -0.22 (95% CI -0.25 to -0.19), standardized effect d = -2.06; z-test p = <0.001.
• AVP-923-20: mean 0.24 versus 0.47 on control; difference -0.23 (95% CI -0.26 to -0.20), standardized effect d = -2.20; 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.

Mean Change From Baseline at Day 84 in Beck Depression Inventory (BDI-II) Total Score

• 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:
  • AVP-923-30: mean -1.59 versus -0.02 on control; difference -1.57 (95% CI -3.11 to -0.03), standardized effect d = -0.27; z-test p = 0.046.
  • AVP-923-20: mean -1.03 versus -0.02 on control; difference -1.01 (95% CI -2.55 to 0.53), standardized effect d = -0.17; z-test p = 0.199.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AVP-923-30 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AVP-923-20 and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline to Day 84 in Pain Rating Scale (PRS) of MS Subjects

• 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:
  • AVP-923-30: mean -1.00 versus -0.40 on control; difference -0.60 (95% CI -1.63 to 0.43), standardized effect d = -0.24; z-test p = 0.255.
  • AVP-923-20: mean -0.70 versus -0.40 on control; difference -0.30 (95% CI -1.26 to 0.66), standardized effect d = -0.13; z-test p = 0.539.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AVP-923-30 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AVP-923-20 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover two distinct outcome areas: depressive symptoms measured by the Beck Depression Inventory and pain ratings among participants with MS. Across these results, the active-arm estimates generally point toward a larger decrease in the score than placebo, but the precision is mixed. One of the unadjusted Beck Depression Inventory comparisons has a confidence interval excluding zero; the other does not. Both pain-rating comparison intervals include zero. This overall pattern is less definitive than the primary endpoint’s sponsor-reported comparisons.

The secondary outcomes address different aspects of participants’ reported health and should not be treated as alternate measurements of PBA episode frequency. Their relation to the primary result is therefore contextual: they may add information about other measured outcomes, but they neither reproduce the primary endpoint nor establish why its estimates differ between treatment and placebo. The registry lists additional secondary outcomes, including CNS-LS, NPI-Q, and SF-36 measures, but their numerical results are not reported in the registry record.

The registry gives no adjusted sponsor analysis for the two secondary outcomes with posted numerical summaries. The comparisons described in the summaries are unadjusted recalculations. General statistical caution: when multiple outcomes and treatment comparisons are examined, the chance of at least one apparently notable result can increase if no multiplicity procedure is used. The registry does not report whether the secondary analyses were prespecified in a hierarchy or whether any adjustment was made. Accordingly, an isolated unadjusted p-value should carry less weight than a prespecified primary analysis, and should be interpreted alongside the full set of outcomes, uncertainty intervals, and analysis details.

The registry does not report a secondary-outcome analysis plan in enough detail to establish whether these results were confirmatory or exploratory. These summaries can describe the posted findings, but the record does not support treating them as definitive evidence across all listed secondary domains.

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

• Mean Change From Baseline in CNS-LS Total Score by Visit
• Mean Change From Baseline to Day 84 in Neuropsychiatric Inventory (NPI-Q) Frequency and Severity Score (EE Population)
• Mean Change From Baseline to Day 84 in Neuropsychiatric Inventory (NPI-Q) Frequency and Severity Score (ITT Population)
• Mean Change From Baseline at Day 84 in SF-36 (Short-Form) Health Survey Medical Outcome Score by Category
• Mean Change From Baseline at Day 84 in Beck Depression Inventory (BDI-II) Total Score
• Mean Change From Baseline to Day 84 in Pain Rating Scale (PRS) of MS Subjects

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a repeated count outcome: episodes were counted each day and entered in a diary. The stated endpoint compares the rate over the 84-day treatment period with the baseline rate. Because it is a ratio, the value 1 represents equal estimated rates across those periods; a value below 1 represents a lower estimated rate during treatment, and a value above 1 represents a higher estimated rate. This is a general interpretation of a rate ratio, not a separate claim about the clinical importance of any particular value.

Why use longitudinal negative binomial regression?

Longitudinal analysis can use repeated observations over time rather than reducing each participant’s diary to a single unstructured observation. The registry identifies negative binomial regression and says that the primary outcome was adjusted for study site and underlying disease. In general, negative binomial regression is useful for count outcomes when variability exceeds what a Poisson model would expect. This extra variability is called over-dispersion. Accounting for it can produce uncertainty estimates that better reflect the observed spread in counts, provided the model is suitable for the data.

The registry does not report the model formula, the exact repeated-measures structure, the link function, or diagnostics. It does not report whether other covariates were included or how data from participants with incomplete follow-up contributed. Therefore, the model can be described at the level recorded in the registry, but its implementation cannot be independently reconstructed from the summary alone.

What do the adjusted estimates represent?

The reported primary arm values are least-squares means for the episode-rate ratio, with 95% confidence intervals. The endpoint description says the estimates were adjusted for site and underlying disease. The sponsor’s comparisons are reported as ratios of episode-rate reduction ratios, also from longitudinal negative binomial regression. A ratio of reductions compares the estimated treatment-related reductions between groups. It is not the same quantity as the difference between two arm-level post-to-pre ratios.

General statistical interpretation: adjustment accounts for specified factors in the model and can improve comparability or precision when handled appropriately. It does not guarantee that all potential sources of bias have been removed. The registry does not report the adjustment details beyond study site and underlying disease, nor whether the model’s assumptions were checked.

What do the unadjusted recalculations add?

The posted recalculations compare the arm-level summaries with the placebo summary using simple unadjusted methods. For the primary endpoint, the reported recalculated mean differences are -0.218 and -0.228, with p-values below 0.001. These calculations do not reproduce the sponsor’s longitudinal regression model, its adjustments, or its ratio-of-reduction comparison. They are a secondary way to examine the posted summaries, not a replacement for the sponsor’s analysis.

The recalculated confidence intervals and standardized effect summaries depend on the posted values and the stated calculation approach. For the primary outcome, the standard deviations used in the recalculation are approximated from standard errors, as indicated in the record. This approximation is another reason to keep the recalculation distinct from the trial’s own regression analysis. It should not be read as an independent validation using participant-level data.

How should p-values and confidence intervals be read?

A p-value describes how incompatible the observed data are with a specified null hypothesis, under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not express the chance that the result will be reproduced. The sponsor reports p-values below < 0.001 for the primary comparisons, while the simple recalculations report p-values below 0.001. The difference in thresholds reflects the separate reported analyses; the values should not be treated as interchangeable.

A confidence interval gives a range of estimates compatible with the data and method at the stated confidence level. Narrower intervals indicate greater statistical precision under that method. The primary arm intervals are relatively narrow as reported, but interval width alone does not address systematic bias, missing data, model misspecification, or clinical importance. The registry’s summary is not sufficient to evaluate all of those issues.

The secondary continuous outcomes are reported as mean changes with standard deviations. Their unadjusted recalculations use differences in group means and confidence intervals. General interpretation: a confidence interval that includes zero does not establish that the groups are identical; it indicates that the data and method do not rule out a zero difference at that interval level. Conversely, an interval excluding zero does not by itself establish clinical importance, especially when many outcomes or comparisons are examined.

11. Confidence Intervals and Precision

The primary arm estimates include 95% confidence intervals. AVP-923-30 is reported as 0.247, with an interval from 0.233 to 0.262; AVP-923-20 is 0.237, with an interval from 0.224 to 0.251; and placebo is 0.465, with an interval from 0.441 to 0.489. These intervals describe uncertainty around the adjusted episode-rate ratio estimates under the sponsor’s model. They are not ranges containing the outcome for every participant.

The sponsor also reports 95% confidence intervals for its two comparisons. Their exact endpoints are given to more than three decimal places in the registry, so they are not reproduced. The sponsor’s reported comparison p-values are below < 0.001. Both comparison intervals are reported as bounded away from the null ratio of 1, consistent with the reported tests under the sponsor’s model.

General statistical explanation: an interval’s precision depends on the amount and variability of information in the data, as well as the analysis method. A narrow interval can indicate that an estimate is statistically precise, but it cannot correct for bias or show that the endpoint captures every outcome important to participants. The arm intervals quantify uncertainty in each arm’s estimated rate ratio; they are not themselves the confidence intervals for a direct difference between arms.

The registry does not report confidence intervals for every secondary outcome. For the posted secondary recalculations, the interval for the AVP-923-30 Beck Depression Inventory comparison excludes zero, while the interval for AVP-923-20 includes zero. Both posted pain-rating comparison intervals include zero. Those distinctions describe statistical precision for these unadjusted comparisons, not proof of presence or absence of an effect.

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 figures are illustrations based on the observed effect, not the original trial’s sample-size design. For these continuous outcomes, the figures are participants per arm. The sample-size 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 as the stated fraction of the observed effect. The registry’s note says that time-to-event planning figures, if present, would instead be total event counts; the outcomes are not time-to-event outcomes.

The 80% power column gives the illustrative participants per arm for an analysis with an 80% chance of detecting the chosen effect if that effect is real and the assumptions hold. The 90% power column gives the corresponding number for a 90% chance under those assumptions. These are planning concepts, not probabilities that the trial result is correct. The registry’s own original design assumptions and sample-size justification are not reported in the registry record.

Rows for a smaller fraction of the observed effect require more participants per arm than rows using the full observed effect. This is the usual relationship: smaller differences are harder to distinguish from sampling variation, so more information is needed to detect them at a given significance level and power target. The displayed values are sensitive to the observed effect and variability used in the illustration, and should not be carried over as definitive requirements for a future study without a separate design calculation.

This is not observed power. It is a planning illustration calculated from the posted summaries and assumptions, and it does not tell whether the completed trial had a particular probability of success after its results were observed.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.218; pooled standard deviation σ = 0.106.
2. n = 2 × (1.96 + 0.842)² × 0.106² / -0.218² = 3.7, rounded up to 4 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
delta <- -0.218                      # observed difference in means
sigma <- 0.10563313273844                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(573443)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 4 (80% power), 5 (90% power)
 75% of observed effect: n per arm = 7 (80% power), 9 (90% power)
 50% of observed effect: n per arm = 15 (80% power), 20 (90% power)
power.t.test: 4.9 
Simulated power at n = 4 per arm: 0.681 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s primary analysis used longitudinal negative binomial regression and compared each AVP-923 dose with placebo using the ratio of episode-rate reduction ratios. The registry reports estimates, 95% confidence intervals, and p-values below < 0.001 for both dose comparisons. This is the trial’s reported comparative analysis and should be distinguished from the simple recalculations based on arm summaries.

The recalculations give unadjusted mean differences of -0.218 for AVP-923-30 versus placebo and -0.228 for AVP-923-20 versus placebo, with p-values below 0.001. These are not estimates of the sponsor’s ratio-of-reductions parameter. They also do not include the stated adjustment for study site and underlying disease or the longitudinal regression structure.

The registry does not flag a discrepancy between the sponsor’s analysis and the recalculations. That does not make the estimates interchangeable: they answer related but different statistical questions. The sponsor’s model-based comparisons are the appropriate results to cite as the trial’s own primary analysis. The recalculations can provide a simple, unadjusted view of the posted arm summaries, but cannot independently reproduce the sponsor’s analysis without participant-level data and full model details.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports two primary sponsor comparisons, one for each AVP-923 dose against placebo, as well as multiple secondary outcomes. It does not report whether the primary comparisons were controlled for multiplicity, whether one dose was designated as the principal comparison, or whether a testing hierarchy was specified. Adjustment for multiple comparisons and the prespecified testing strategy are therefore not reported in the registry record.

The record lists seven outcome measures and includes results for the primary outcome and some secondary outcomes. It does not provide a complete numerical result for every listed secondary outcome. It also does not report how many analyses were planned, how outcome selection was handled, or whether analyses not posted were conducted. Without this information, the effect of selective reporting or repeated testing cannot be assessed from the registry summary alone.

The primary population is identified as intent-to-treat, with the definition referring to all randomized subjects in the double-blind phase and all enrolled subjects in the open-label extension phase. The registry does not report the exact analysis counts for each endpoint, whether all randomized participants contributed usable diary data, or how participants with missing baseline or follow-up records were handled.

Missing-data procedures are not reported in the registry record. In particular, the record does not say whether missing diary days were imputed, whether incomplete follow-up was handled through the regression model, or whether sensitivity analyses tested alternative assumptions. This matters because repeated diary counts may be incomplete, and the assumptions used for incomplete observations can influence both estimates and uncertainty.

Interim analyses, stopping rules, and a detailed statistical analysis plan are not reported in the registry record. Their absence from the record does not establish that they were absent from the conduct of the trial; it means their role cannot be evaluated from the information posted.

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: respiratory failure (2.7%), dysphagia (1.8%), deep vein thrombosis (1.8%), pulmonary embolism (0.9%), respiratory depression (0.9%).

For the double-blind groups, the registry reports serious adverse events affecting 8 of 110 participants in AVP-923-30, 9 of 107 in AVP-923-20, and 10 of 109 in placebo. The open-label AVP-923-30 group reports 14 of 253 participants affected. These are participant counts with at least one serious adverse event as recorded in the registry summary; they are not counts of all serious events.

The registry also reports other adverse events affecting 66 of 110 participants in AVP-923-30, 65 of 107 in AVP-923-20, 63 of 109 in placebo, and 123 of 253 in the open-label group. The death counts are not reported in the registry record. The listed serious-event terms include respiratory failure (2.7%), dysphagia (1.8%), deep vein thrombosis (1.8%), pulmonary embolism (0.9%), respiratory depression (0.9%), and bronchospasm (0.9%).

These summaries do not establish that an event was caused by a study treatment, and they do not provide event timing, duration, recurrence, or participant-level context. The open-label group is also not a randomized placebo comparison. Safety interpretation should therefore remain descriptive of the counts and terms recorded, rather than attributing events or comparing risk beyond what the registry reports.

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

The primary results describe episode-rate estimates over treatment relative to baseline and sponsor comparisons against placebo. The arm-level estimates are below 1 in all three groups, and the sponsor reports separate adjusted comparisons for each AVP-923 dose against placebo. The posted data therefore describe differences in estimated episode-rate patterns across the randomized groups under the stated model.

They do not show that every participant experienced a reduction, nor do group averages describe an individual participant’s likely experience. A rate ratio is a summary of counts over periods; it does not identify the number or timing of episodes for any one person. The registry summary also does not give a threshold for a change considered important to participants, so statistical estimates alone cannot establish the practical or clinical importance of the differences.

The reported primary analysis is adjusted for study site and underlying disease, but the record does not provide participant-level data, complete model details, or missing-data procedures. The primary findings should therefore be understood as registry-reported model-based estimates, not as a result that can be fully audited or independently reconstructed from the summary values.

Secondary outcomes are less consistent in precision, and some listed outcomes do not have numerical results in the registry record. These data do not establish a broad effect across all measured health domains. Nor do the posted results explain the biological mechanism or establish whether the same estimates apply equally to the ALS and MS populations.

These findings are statistical descriptions of this completed trial’s posted outcomes. They are not medical advice, a substitute for individual clinical assessment, or a guarantee about outcomes outside the studied population and follow-up period. The registry does not report longer-term controlled results for the primary endpoint.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint and comparison estimand matter. The primary endpoint is a post-to-pre rate ratio, whereas the sponsor’s comparative result is a ratio of episode-rate reduction ratios. The simple recalculations use differences between arm-level summaries. These quantities are related, but they are not the same statistic; treating them as interchangeable would obscure what each analysis estimates.

It also shows the role of a model suited to repeated counts. Daily diary episodes are counts recorded over time, and longitudinal negative binomial regression can address repeated observations and extra variability under its assumptions. Adjustment for study site and underlying disease is part of the sponsor’s stated approach. Readers still need model details and diagnostics to judge how well those assumptions fit the data, and those details are not reported in the registry record.

Confidence intervals help distinguish an estimate from its uncertainty. The reported primary arm intervals are narrow, while some secondary comparisons are less precise. Statistical significance, interval width, and clinical importance answer different questions: a small p-value does not quantify importance, and a narrow interval does not address bias or incomplete reporting.

Finally, the registry provides an opportunity to compare trial-reported analysis with transparent calculations from summary statistics. The recalculations are useful as a limited cross-check, but they cannot reproduce a regression analysis or replace its prespecified methods. Planning illustrations likewise describe hypothetical sample-size requirements under stated assumptions; they are not the original design rationale or post hoc evidence of power.

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.

The registry summary does not include the protocol or a detailed statistical analysis plan. The original sample-size justification, planned power, allocation procedures, and interim-analysis arrangements are not reported in the registry record. This limits assessment of whether the posted analyses match the original plan.

Primary episode counts came from daily diaries, but the record does not explain how missing diary entries or incomplete follow-up were handled. The exact model structure and diagnostics are also not reported. Consequently, the published summary does not permit independent verification of the sponsor’s regression estimates or of the assumptions supporting their confidence intervals.

The primary population description refers both to randomized double-blind participants and to enrolled participants in an open-label extension. The record does not clarify how the extension population relates to the primary efficacy comparisons. It also does not provide subgroup-specific results for ALS and MS, despite including both conditions in the study population.

Only some secondary outcomes have numerical results in the registry record. Multiplicity procedures and the confirmatory status of secondary analyses are not reported. This makes isolated secondary p-values difficult to interpret as definitive findings. The simple recalculations are also based on summary statistics, and the primary outcome’s recalculated standard deviations are approximate; these calculations cannot account for participant-level correlations or reproduce the adjusted longitudinal model.

Safety results are presented as affected-participant counts and selected event terms. Event timing, causal attribution, recurrence, and death counts are not reported in the registry record. The open-label safety group lacks a concurrent randomized comparator in the posted summary. These limitations constrain interpretation of safety patterns across groups.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of AVP-923 in PBA Patients With ALS or MS — NCT00573443.
• Registry record last updated 2017-04-12; status last verified 2017-03.
• Results first posted 2013-07-10.
• 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

This completed Phase 3 study randomized 326 participants with PBA associated with ALS or MS to AVP-923-30, AVP-923-20, or placebo. The regimens began once daily and then continued twice daily during a 12-week treatment period. The primary endpoint was the treatment-period episode rate relative to baseline, adjusted for study site and underlying disease using longitudinal negative binomial regression.

The sponsor reported adjusted comparisons of each dose with placebo. The posted arm estimates were below 1 for both active regimens and placebo. Unadjusted recalculations from the arm summaries are separate from the sponsor’s regression analysis and should not be read as reproducing it.

The registry includes selected secondary and safety summaries, but does not report complete numerical results for all listed secondary outcomes, missing-data methods, multiplicity procedures, or the original sample-size justification. These omissions limit assessment of the full analysis plan and the broader pattern of outcomes.