A Study for the Treatment of Alcohol Dependence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study for the Treatment of Alcohol Dependence (NCT00804570), a randomized phase 2 study. The primary outcome is Percentage of Heavy Drinking Days at Week 16 Endpoint.

2. Clinical Question

The registry record describes a randomized parallel-group study in alcohol dependence. Its primary objective was to test whether LY2196044 could reduce the number of heavy drinking days per month. The posted primary outcome is expressed as change in percentage of heavy drinking days at the Week 16 endpoint, rather than as a monthly count.

The comparison is between treatment groups, not a test of whether either group changed from its own baseline in isolation. Both posted group estimates are changes from baseline, and the central statistical question is whether the mean change differed between assigned groups after the specified model adjustments. A negative change indicates a reduction in the percentage of heavy drinking days under the outcome’s direction of measurement. The registry’s description defines heavy drinking by sex-specific daily drink thresholds, and the drinking assessment used the Timeline Followback Method.

The primary analysis population is described as participants with a baseline and post-baseline value. The registry record does not report additional details about who was eligible, the detailed handling of participants who discontinued, or the original rationale for the enrollment target. Consequently, the clinical question can be described from the posted endpoint and treatment comparison, but not expanded into claims about unreported eligibility criteria or design decisions.

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group study comparing LY2196044 with placebo. The registry record reports enrollment of 375 and status as completed. The study started in 2008-11, and primary completion was recorded in 2010-02. The planned treatment period is described as 16 weeks, after a screening and assessment period that included medication washout.

Random allocation is intended to make treatment groups comparable, on average, with respect to factors that could affect outcomes. Masking can reduce the influence of treatment knowledge on participant behavior, care, and outcome assessment. The record labels masking as triple but does not specify which roles were masked, so the precise masking arrangement is not reported in the registry record. The parallel design means participants were assigned to a treatment group rather than described as switching between treatments.

The posted primary outcome analysis involved 181 participants in the LY2196044 group and 172 in the placebo group. These are the group counts for that outcome analysis, which required baseline and post-baseline values; they should not be confused with the enrollment figure. Other outcomes have different analysis counts. The registry record does not describe the reasons for these differences or provide a full participant-flow account in the information reported for this analysis.

The primary endpoint was analyzed using least-squares means and a mixed models analysis. The endpoint description lists adjustments for treatment, pooled investigator, visit, gender, family history, treatment-by-visit, gender-by-family-history, baseline, and baseline-by-visit, and states that an unstructured covariance structure was used. Detailed implementation choices beyond those listed, including the original statistical analysis plan, 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants with a baseline and post-baseline value.

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 Heavy Drinking Days at Week 16 Endpoint, measured over Week 16.

The primary outcome is percentage of heavy drinking days at the Week 16 endpoint, expressed as change from baseline in the posted group estimates. The Timeline Followback Method assesses daily drinking with a calendar covering a specified period. For this study, a heavy drinking day was defined as a day with at least 4 drinks for women or at least 5 drinks for men. The registry describes the primary objective in terms of reducing the number of heavy drinking days per month, while the posted endpoint expresses the measure as a percentage of days.

This outcome captures the frequency of days meeting a prespecified drinking threshold. It is different from measures of average drinks per day or the amount consumed on a drinking day: those can change without an identical change in the proportion of days classified as heavy drinking. The measure therefore focuses on a behavior directly tied to the study’s definition of heavy drinking, rather than total alcohol consumption alone.

The posted least-squares mean is a model-adjusted estimate, not simply the raw average of observed participant changes. The model accounts for the covariates and repeated-measure structure listed in the outcome description. A change below zero represents a decrease in the percentage of heavy drinking days from baseline. The between-group estimate is the comparison relevant to the randomized treatment question; a change within either group by itself does not isolate a treatment effect.

The analysis population is described as participants with a baseline and post-baseline value. The registry record does not report further details about the calendar assessment window used to form the Week 16 endpoint or the handling of unavailable assessments.

7. Results Posted in the Registry

• LY2196044: mean -43.02 versus -38.72 on control; difference -4.30 (95% CI -10.13 to 1.53), standardized effect d = -0.15; z-test p = 0.149.

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 From Baseline in Drinks Per Day at Week 16 Endpoint

• 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 errors.
• Result:
  • LY2196044: mean -5.37 versus -4.66 on control; difference -0.71 (95% CI -1.32 to -0.10), standardized effect d = -0.24; z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LY2196044 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Percentage of Days Abstinent at Week 16 Endpoint

• 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 errors.
• Result:
  • LY2196044: mean 33.49 versus 28.12 on control; difference 5.37 (95% CI -0.37 to 11.11), standardized effect d = 0.20; z-test p = 0.067.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LY2196044 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Drinks Per Drinking Day at Week 16 Endpoint

• 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 errors.
• Result:
  • LY2196044: mean -3.77 versus -3.38 on control; difference -0.39 (95% CI -1.11 to 0.33), standardized effect d = -0.11; z-test p = 0.289.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LY2196044 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the picture beyond the primary measure. They include changes in drinks per day, percentage of days abstinent, drinks per drinking day, drinks per heavy drinking day, drinking-related scales and consequences, and laboratory measures. The posted subset with comparative estimates includes outcomes that capture both frequency and quantity of drinking. This breadth is useful for describing related domains, but these measures are not interchangeable: an improvement in one does not necessarily imply the same pattern in another.

Across the secondary comparisons with estimates, the evidence is mixed rather than uniformly aligned. Some unadjusted comparisons have intervals excluding zero, while others include zero. The pattern does not amount to consistent statistical confirmation across all the related outcomes. It also does not overturn the primary endpoint interpretation: the prespecified central question concerns the percentage of heavy drinking days at Week 16, and that model-based comparison has an interval including zero.

Secondary endpoints can help identify signals, assess whether changes appear across related measures, and motivate further study. However, the registry lists many secondary outcomes, and multiplicity adjustment is not reported in the registry record. When many outcomes are examined, some may appear notable by chance even if there is no underlying effect for those outcomes. Unadjusted secondary p-values therefore deserve less weight than a primary result interpreted according to its study analysis.

The posted secondary estimates also have outcome-specific analysis populations and model details, so differences in their apparent strength cannot be attributed solely to treatment effects. The overall pattern is best treated as supportive context and hypothesis-generating evidence, not as a collection of independent confirmatory findings. Specific secondary estimates and their uncertainty should be read on their own scales rather than combined into a single overall claim.

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

• Change From Baseline in Drinks Per Day at Week 16 Endpoint
• Change From Baseline in Percentage of Days Abstinent at Week 16 Endpoint
• Change From Baseline in Drinks Per Drinking Day at Week 16 Endpoint
• Change From Baseline in Drinks Per Heavy Drinking Day at Week 16 Endpoint
• Change From Baseline in Obsessive Compulsive Drinking Scale (OCDS) Total Score at Week 16 Endpoint
• Change From Baseline in Drinker Inventory of Consequences (DrInC) - Recent Consequences (DrInC-2R) Total Score at Week 16 Endpoint
• Ratio of Geometric Means Over Baseline in Gamma-Glutamyltransferase (GGT) Level at Week 16 Endpoint
• Ratio of Geometric Means Over Baseline in Percent Carbohydrate-Deficient Transferrin (%CDT) Level at Week 16 Endpoint

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical explanation: A randomized comparison estimates how outcomes differ between assigned groups. The group-level changes describe what happened during the study in each arm, while the between-group contrast addresses whether the changes differed. A within-group decrease is not, by itself, evidence that the assigned treatment caused that decrease; changes may also reflect time, study participation, or other influences shared by groups.

The primary endpoint uses least-squares means. In general, a least-squares mean is an estimate from a statistical model that accounts for specified variables, rather than an unadjusted arithmetic average. The registry says the primary model controlled for treatment, pooled investigator, visit, gender, family history, treatment-by-visit, gender-by-family-history, baseline, and baseline-by-visit. This adjustment is intended to estimate group outcomes while accounting for those model terms. The registry record does not provide further detail about coding choices, model diagnostics, or all implementation decisions.

The endpoint description states that an unstructured covariance structure was used. In general, a covariance structure describes how repeated observations from the same participant are related across visits. An unstructured choice allows the model to estimate the relationships among repeated measurements without imposing a simple pattern. This can be flexible, but its suitability depends on the available data and model implementation. The registry record does not report diagnostic results or alternative covariance analyses.

The reported mixed models analysis gives a mean difference in final values, a confidence interval, and a p-value. The registry’s outcome description calls the arm estimates least-squares means for change from baseline, while the reported analysis labels its contrast as a mean difference in final values. The record does not explain that terminology further. The sponsor’s reported estimate and inferential statistics are therefore best read as the study’s own model-based comparison, with the posted outcome description supplying the endpoint context.

General statistical explanation: A standard error describes the estimated sampling uncertainty of a statistic under its model. It is not the spread of individual participant outcomes. The primary arm estimates have standard errors of 2.09 and 2.12. Their precision relates to the estimated group means; the uncertainty of the group contrast also depends on the model and covariance information. The arm standard errors should not be mistaken for standard deviations.

A confidence interval gives a range of values compatible with the estimate under the model and its assumptions. The sponsor’s 95% interval for the primary contrast extends from -9.72 to 1.13. Since zero is within this interval, the data do not provide a conventionally statistically significant result for a two-sided test at the 0.05 level. A p-value measures how unusual data at least this discrepant would be under a specified null hypothesis and model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance.

The posted unadjusted re-calculations use summary statistics to form a simple comparison. They are labeled re-calculated because they are not the original model output. In this analysis, the re-calculated primary contrast is -4.3, and its unadjusted p-value is 0.149. The sponsor’s model-based result is -4.30 with p = 0.120. The estimates are similar in direction and magnitude, but the exact inferential results differ because the re-calculation does not reproduce the study’s mixed model. The registry record does not report a discrepancy flag as true.

The planning illustrations are based on the observed effect and stated assumptions: two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting 100%, 75%, or 50% of the observed effect. In general, smaller target effects require more participants to distinguish them from random variation at the same significance level and power. These are planning calculations rather than retrospective measures of how likely the completed trial was to succeed.

The primary analysis population is participants with a baseline and post-baseline value. This is a defined analysis subset, not necessarily every randomized participant. In general, restricting analysis to participants with observed outcome data can affect interpretation if missingness is related to outcomes or treatment. The record does not report the amount, reasons, assumptions, or sensitivity analyses for missing data, so the direction or size of any such effect cannot be assessed from the reported information.

The trial posted multiple secondary outcomes, including measures of drinking quantity, abstinence, drinking intensity, and consequences, as well as laboratory measures. In general, testing many outcomes increases the chance that at least one result appears statistically notable by chance. Multiplicity methods can address this issue, but whether one was used is not reported in the registry record. Unadjusted secondary p-values therefore do not carry the same confirmatory weight as a prespecified primary analysis with an explicit multiplicity plan.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a mean difference of -4.30, with a 95% confidence interval from -9.72 to 1.13. The interval includes zero, so the posted data are compatible with no between-group difference as well as with a difference in either direction. Its width indicates that the point estimate is not precise enough to pin down a narrow range of plausible effects. The p-value is 0.120.

The interval should be interpreted on the outcome’s scale: percentage of days. The point estimate favors a greater reduction in the LY2196044 group, but the upper end of the interval is above zero. Thus the estimate’s direction alone does not settle whether there is a difference, and the interval should not be read as a range containing a fixed proportion of individual participant responses. It describes uncertainty about the estimated group contrast under the analysis model.

The unadjusted re-calculation gives an estimate of -4.3 and an interval that includes zero. Its p-value is 0.149. The sponsor’s model uses the study analysis approach, whereas the re-calculation is derived from posted summary statistics. The difference between their reported inferential results is a reminder that standard errors and intervals can depend on analysis methods, covariate adjustment, and repeated-measure modeling. The registry record does not identify a discrepancy requiring the sponsor result to be set aside.

Confidence intervals address statistical uncertainty, not clinical importance. The registry record does not state a threshold for a clinically important difference on this endpoint, so the interval cannot be classified against such a threshold. It also does not report a sample-size justification or precision target for the original design. The posted estimate and interval are the appropriate basis for describing the observed precision, without inferring what the trial was designed to detect.

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 participants per arm, not total participants and not total events, because this is a continuous-outcome comparison. They are illustrations calculated from the observed effect, not a report of the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The original design assumptions are not reported in the registry record.

The 80% power column describes the planning number of participants per arm associated with an 80% chance of detecting the target effect under those assumptions, if the assumptions hold and the target effect is real. The 90% power column gives the corresponding planning number for a 90% chance. These are design-stage operating characteristics, not promises about the result of a future study.

The rows describe planning for 100%, 75%, and 50% of the observed effect. As the target effect becomes smaller, it is harder to distinguish from random variation, so the planning requirement rises. For the primary outcome, the illustration based on 100% of the observed effect gives 664 participants per arm for 80% power and 889 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,181 participants per arm for 80% power and 1,581 participants per arm for 90% power. Planning for 50% gives 2,656 participants per arm for 80% power and 3,556 participants per arm for 90% power.

These values depend on the observed effect used as their starting point, as well as the stated assumptions. They should not be interpreted as evidence that the completed study had a particular probability of detecting its result. This is not observed power.

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 = -4.300; pooled standard deviation σ = 27.965.
2. n = 2 × (1.96 + 0.842)² × 27.965² / -4.300² = 664.0, rounded up to 664 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 <- -4.3                      # observed difference in means
sigma <- 27.9652812223685                     # 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(804570)
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 = 664 (80% power), 889 (90% power)
 75% of observed effect: n per arm = 1,181 (80% power), 1,581 (90% power)
 50% of observed effect: n per arm = 2,656 (80% power), 3,556 (90% power)
power.t.test: 664.9 
Simulated power at n = 664 per arm: 0.793 (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 reported primary analysis is the mixed models analysis: mean difference -4.30, 95% confidence interval -9.72 to 1.13, and p = 0.120. This is the study’s own reported inferential result and should be distinguished from the simple unadjusted re-calculation based on posted summary statistics.

The re-calculated estimate is -4.3, with an unadjusted p-value of 0.149 and an interval that includes zero. Its direction and broad interpretation align with the sponsor result: the estimated difference is negative, but the interval includes no difference. The two analyses are not identical methods. The re-calculation does not reproduce the specified mixed model, its covariate adjustment, or its repeated-measure covariance structure, so its p-value and interval are supplementary checks rather than substitutes for the sponsor’s analysis.

The registry record does not flag a discrepancy as true. Accordingly, there is no recorded conflict requiring the sponsor analysis to be displaced by the re-calculation. The primary conclusion should be framed around the sponsor’s model-based estimate and its uncertainty, while the re-calculated result illustrates how a simpler summary-statistic comparison behaves.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 27 outcome measures and 29 analyses, including the primary endpoint and many secondary outcomes. Examining multiple outcomes creates a multiplicity concern: even when all null hypotheses are true, repeated testing can make one or more nominally small p-values more likely to occur by chance. The registry record does not report whether the study used a formal multiplicity adjustment, a hierarchy among outcomes, or another strategy to control the overall false-positive risk.

The primary endpoint remains the clearest focus because it is identified as the primary outcome and is tied to the stated study objective. The posted secondary results should be interpreted more cautiously where their p-values are unadjusted. The registry record does not report enough detail to determine whether the posted secondary tests were prespecified in a formal analysis plan or how their results were intended to affect confirmatory conclusions.

For missing data, the primary population is described as participants with a baseline and post-baseline value. The primary outcome analysis counts are 181 for LY2196044 and 172 for placebo, while enrollment is reported as 375. These figures describe different aspects of the record and do not establish why participants are absent from a particular analysis. The registry record does not report the amount or pattern of missing primary outcome data, reasons for missingness, assumptions about missing outcomes, or sensitivity analyses.

In general, missing-data methods rely on assumptions about how unavailable measurements relate to observed information and outcomes. If those assumptions are not stated, the robustness of an estimate to missingness cannot be assessed from the registry record. The record also does not report a full analysis-population definition beyond the baseline and post-baseline requirement, or whether another population was used as a sensitivity analysis.

Consequently, the primary estimate can be described as the posted model result for its stated analysis population, but the available information does not support claims about the effect of multiplicity procedures or the robustness of the result to missing-data assumptions. These omissions are limitations in interpreting the statistical plan, not evidence that a particular procedure was or was not used.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: small intestinal obstruction (0.5%), biliary colic (0.5%), appendicitis (0.5%), alcohol detoxification (0.5%), cholecystitis (0.5%).

The registry record reports serious adverse events for 4 participants at risk of 187 in the LY2196044 group and 5 participants at risk of 188 in the placebo group. It separately reports other adverse events for 143 participants at risk of 187 in the LY2196044 group and 116 participants at risk of 188 in the placebo group. These are descriptive counts, and the safety denominators differ from the primary outcome analysis counts.

The record lists serious-event terms including small intestinal obstruction, biliary colic, appendicitis, alcohol detoxification, cholecystitis, and muscle strain, each reported as 0.5%. Those terms are not evidence on their own that the events were caused by study treatment. The registry does not provide detailed event narratives, timing, severity beyond the serious classification, or treatment-relatedness assessments in the information used for this summary.

Deaths are not reported in the registry record. Counts alone cannot establish comparative safety, especially without further information about event definitions, follow-up, exposure, and statistical assessment. The figures should therefore be read as recorded safety events during the study, not as a causal estimate of treatment risk.

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

The primary result estimates the difference between LY2196044 and placebo in change in percentage of heavy drinking days at Week 16. The sponsor’s adjusted estimate is -4.30, with a 95% confidence interval from -9.72 to 1.13 and p = 0.120. This describes a point estimate in the direction of a greater decrease with LY2196044, but the interval includes zero. The posted analysis therefore does not establish a statistically clear between-group difference on this primary outcome.

This does not demonstrate that the treatments are equivalent, nor does it prove that there is no effect. A result that is not statistically significant can reflect a genuinely small difference, uncertainty in the estimate, or both. The interval expresses that uncertainty, and the registry record does not give a threshold for interpreting the clinical importance of a difference in this measure.

The result applies to the recorded outcome, time point, analysis population, and model. It does not by itself answer whether treatment affects other aspects of alcohol dependence, longer-term outcomes, or populations not represented in the study. The posted secondary outcomes cover additional drinking-related and laboratory measures, but multiplicity procedures are not reported, so isolated secondary findings should not be treated as equivalent to confirmation of the primary objective.

The safety counts are also limited in scope. They describe recorded adverse events, but do not establish causation or provide a complete benefit-risk assessment. Overall, the record supports a precise description of the primary estimate and its uncertainty, while leaving important questions about clinical importance, missing-data robustness, and broader applicability unresolved.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment-group contrast matters more than noting that both groups improved from baseline. The posted primary group estimates are both negative, but the clinical question is whether their changes differed. The sponsor’s model-based contrast is negative, yet its confidence interval includes zero. The point estimate’s direction and the statistical uncertainty must be considered together.

It also highlights the difference between an adjusted model result and a simple re-calculation from summary statistics. The sponsor analysis uses a mixed model and the covariates and repeated-measure structure listed in the record. The re-calculation is a useful unadjusted check, but it does not recreate the study’s fitted analysis. Understanding which estimate answers the study’s planned question is central to responsible interpretation.

The secondary outcomes show why multiplicity and outcome hierarchy matter. A study can examine several related domains, but a nominally notable result among many outcomes should not automatically be treated as confirmatory. The primary endpoint provides the clearest link to the stated objective, while secondary findings can add context and generate questions for future research.

Finally, the planning illustrations distinguish prospective design calculations from retrospective judgments about power. They show how a smaller target effect requires more participants under the stated assumptions, but do not explain the original enrollment target or the completed study’s probability of success. Statistical interpretation is strongest when estimates, uncertainty, analysis choices, missing data, and study design are kept distinct.

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 record does not report the original sample-size justification or the assumptions used to select enrollment of 375. The planning illustrations are based on the observed effect and cannot be treated as evidence of the trial’s original design rationale. The record also does not report a prespecified clinically important difference for the primary endpoint, limiting interpretation of whether the estimated contrast would matter clinically.

The primary analysis includes participants with a baseline and post-baseline value, but details about missing outcome data, reasons for missingness, and sensitivity analyses are not reported in the registry record. This limits assessment of whether the result is robust to incomplete outcome data. The record also does not provide a full participant-flow description in the information summarized for this analysis.

Although the primary outcome description lists adjustment terms and an unstructured covariance structure, the statistical analysis plan, model diagnostics, and further implementation details are not reported. The sponsor’s reported result is available, but its label of mean difference in final values is not explained alongside the change-from-baseline endpoint description. A simple re-calculation cannot resolve such model-specific details.

Multiplicity handling for the many listed outcomes is not reported in the registry record. The secondary results therefore have limited confirmatory interpretation. The safety information is also summarized as event counts and selected serious-event terms, without detailed timing, causality assessment, exposure-adjusted comparisons, or death counts. These constraints do not negate the posted results, but they limit the strength and breadth of conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study for the Treatment of Alcohol Dependence — NCT00804570.
• Registry record last updated 2019-09-24; status last verified 2019-09.
• Results first posted 2017-02-03.
• 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

The registry record describes a completed phase 2 randomized, triple-masked, parallel-group comparison of LY2196044 and placebo for alcohol dependence. Enrollment was 375; the study started in 2008-11 and primary completion was recorded in 2010-02. The planned treatment period was 16 weeks.

The primary endpoint was percentage of heavy drinking days at Week 16, assessed with the Timeline Followback Method. The sponsor’s mixed models analysis reported a mean difference of -4.30, a 95% confidence interval from -9.72 to 1.13, and p = 0.120. The interval includes zero. A simple unadjusted re-calculation also has an interval including zero.

Secondary outcomes span drinking behavior, consequences, and laboratory measures. Multiplicity procedures and detailed missing-data methods are not reported in the registry record. Safety counts are descriptive and do not establish causation. The results are best interpreted as the posted estimates for this study, endpoint, and analysis population, with uncertainty and reporting limitations kept in view.