Craving, Binge Eating and Obesity: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Craving, Binge Eating and Obesity (NCT00414167), a randomized phase 2, phase 3 study. The primary outcome is Frequency of Binge Eating Episodes.

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel-group trial comparing bupropion with placebo. The registry lists phase 2 and phase 3, and names Yale University as the sponsor. The study was marked completed. Its start is recorded as 2005-12, and primary completion as 2011-03. Enrollment was 61.

The medication phase was described as eight weeks of outpatient treatment. The study summary also said participants would have the option of receiving eight weeks of free behavioral weight loss treatment after the medication phase. It describes that treatment as intended to support weight loss and reduce binge eating. The registry does not report how this option was taken up, whether it was part of the primary endpoint assessment, or how its timing was handled in the analysis.

The primary outcome was frequency of binge eating episodes, measured as episodes per week. The primary endpoint timeframe was one week at post treatment. The posted arm summaries include 31 participants for bupropion and 30 for placebo. The primary outcome description specifies baseline forward imputation for missing data. Further information about the analysis population, participant flow, withdrawals, adherence, and handling of other missing observations is not reported in the registry record.

Percent BMI loss was listed as a secondary outcome, with an eight-week timeframe based on baseline and eight weeks. Its posted arm summaries include 31 participants for bupropion and 20 for placebo. The registry does not explain the difference in reported group counts between this outcome and the primary endpoint, so the reason should not be inferred. Detailed eligibility criteria, the original sample-size rationale, and the trial's prespecified 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

Analysis population for the primary outcome, as defined in the registry: Baseline forward imputation for missing data.

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 Frequency of Binge Eating Episodes, measured over One week (at post treatment).

The primary endpoint is the frequency of binge eating episodes, expressed as episodes per week. It is a continuous outcome summarized by the mean and standard deviation. The registry defines the measurement window as one week at post treatment and describes the population for the result as using baseline forward imputation for missing data.

Counting episodes over a defined time window gives a quantitative measure of how often the behavior occurred during that period. Comparing group means can describe the average difference between assigned treatment groups. The mean is useful for conveying the overall level of the outcome, while the standard deviation describes variation among observations within a group. These summaries do not show the full distribution of episode frequencies or how many individuals experienced a particular change.

The posted mean was 0.8 episodes per week for bupropion and 1.0 for placebo. The reported mean difference, defined as bupropion relative to placebo, was -0.2 episodes per week. The endpoint is a post-treatment measurement; the registry description does not provide a separate posted change-from-baseline estimate for binge eating frequency. It also does not report details about the instrument used to record episodes or how reports were collected.

As a general statistical point, a continuous mean is a concise summary, but it can be affected by the spread and shape of the outcome distribution. The registry reports standard deviations of 1.2 and 1.5 for the bupropion and placebo groups, respectively. Those values provide context about variability, but do not by themselves establish whether the mean difference is precise or whether a treatment effect is present. The uncertainty interval and analysis context are needed alongside the group means.

7. Results Posted in the Registry

• Bupropion: mean 0.80 versus 1.00 on control; difference -0.20 (95% CI -0.88 to 0.48), standardized effect d = -0.15; z-test p = 0.566.

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.

Percent BMI Loss

• 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:
  • Bupropion: mean 1.80 versus 0.60 on control; difference 1.20 (95% CI -0.10 to 2.50), standardized effect d = 0.50; z-test p = 0.070.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupropion and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists Percent BMI Loss as a secondary outcome. Its posted means are 1.8 for bupropion and 0.6 for placebo, with reported standard deviations of 2.6 and 2.1. The comparison is a mean difference of 1.2, with a 95% confidence interval from -0.098 to 2.498 and an unadjusted p-value of 0.07. Those values describe the secondary measure and should be interpreted separately from the primary binge-eating endpoint.

Across the outcomes, the primary comparison's point estimate favors bupropion in the direction of fewer binge eating episodes, while the secondary comparison's point estimate favors bupropion in the direction of greater percent BMI loss. Both confidence intervals include zero. This broad pattern does not establish that the outcomes moved together within individual participants, or that one result explains the other. The registry does not report an analysis of the relationship between binge eating frequency and BMI loss.

Secondary outcomes can be useful for describing other aspects of a trial, but they generally provide less confirmatory evidence than the primary endpoint. The primary endpoint is the main outcome designated for the study question, while secondary findings may involve additional comparisons and may not have been the basis for the trial's design. The registry does not report a hierarchy or multiplicity adjustment for these results. As a general statistical matter, testing multiple outcomes without adjustment can make isolated low p-values less persuasive as confirmatory evidence.

The placebo group has 20 participants in the posted BMI-loss result, compared with 30 in the primary outcome summary. The registry does not explain this difference, so its cause cannot be determined from the record. This makes it particularly important not to assume that outcome summaries share identical analysis populations or missing-data handling.

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

• Percent BMI Loss

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary result is a comparison of group means for a continuous endpoint. The mean is the arithmetic average of observed or imputed episode-frequency values in each group. The registry gives the bupropion mean as 0.8 episodes per week and the placebo mean as 1.0. The comparison is expressed as bupropion minus placebo, yielding a mean difference of -0.2 episodes per week. A negative estimate therefore indicates a lower mean in the bupropion group for this endpoint, while a positive estimate would indicate a higher mean.

What does the standard deviation describe?

The standard deviation describes how spread out individual observations are around their group mean. The posted standard deviations are 1.2 for bupropion and 1.5 for placebo. They are not standard errors and are not confidence intervals for the group means. As a general statistical explanation, a standard deviation characterizes variability among observations; a standard error characterizes uncertainty in an estimated quantity, such as a mean or a difference in means.

The posted comparison also gives a pooled standard deviation of 1.356. Pooling is a way to summarize variability across groups for a standardized comparison under assumptions about how the groups' variability should be combined. A standardized effect can express a mean difference relative to a standard deviation, but it does not replace the original-scale result. The original-scale difference remains easier to interpret in episodes per week.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the data under the statistical procedure used. In repeated use of a correctly specified procedure, intervals at the stated confidence level would cover the fixed underlying quantity at the corresponding long-run rate. The primary interval runs from -0.883 to 0.483 episodes per week. Because it extends across zero, the posted estimate is compatible with a negative difference, no difference, and a positive difference within that interval. The interval is not a range containing a stated proportion of individual participants' outcomes.

The registry does not state the model or detailed inferential procedure used for the sponsor's original analysis. The comparison values posted in the record include an unadjusted p-value of 0.566. A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result occurred “by chance.” The posted p-value should be interpreted as unadjusted because the record labels it that way.

Why does missing-data handling matter?

The primary endpoint description states “Baseline forward imputation for missing data.” This means the registry specifies a method for filling in missing outcome values by carrying baseline information forward, but does not provide further detail about implementation. As a general statistical point, an imputation rule can affect group estimates because missing values are replaced by assumptions rather than directly observed post-treatment measurements. The method's suitability depends on why data are missing and how the imputed values relate to the actual outcomes. The registry does not report the amount or pattern of missing primary outcome data, so the influence of imputation cannot be assessed from the posted record.

The registry does not state whether the primary analysis followed an intention-to-treat principle, whether participants were analyzed according to assigned group in all cases, or what other analysis populations were used. Nor does it report protocol deviations or adherence. Those details are relevant to understanding what population and treatment contrast the estimate represents, and should not be inferred from the group summaries alone.

What is the role of the secondary endpoint?

Percent BMI loss is another continuous outcome, summarized by group means and standard deviations. Its posted comparison is also a mean difference, in the units of percent loss. The estimate and confidence interval describe that secondary outcome rather than the primary binge-eating endpoint. The record does not report a formal multivariate model linking the two measures or an analysis of whether changes in one predict changes in the other.

When several outcomes are examined, the chance of at least one apparently notable result can increase if each is tested without accounting for the number of tests. This is a general statistical issue called multiplicity. It does not mean that any particular result is false; it means that unadjusted results across multiple tests warrant more cautious interpretation. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for secondary outcomes.

What cannot be reconstructed from these summaries?

Aggregate means, standard deviations, and group counts do not reveal the individual-level distribution, the presence of influential observations, or the association between baseline and post-treatment measurements. They also do not allow reconstruction of unreported covariate-adjusted analyses. The registry lists zero reported analyses and provides no separate sponsor analysis details, although it does post outcome summaries and comparison estimates. The trial's original statistical analysis plan, model diagnostics, interim analyses, and sample-size justification are not reported in the registry record.

Any recalculated comparisons based on posted summary statistics are simple unadjusted calculations, not a replacement for the trial's own analysis. The registry discrepancy flag is false, so the available record does not indicate a discrepancy that would cause the sponsor's analysis to take precedence. Even so, the lack of detailed analytic methods means the posted summaries should be interpreted as limited evidence about the comparison, not as a complete statistical report.

11. Confidence Intervals and Precision

The primary mean difference is -0.2 episodes per week, and its 95% confidence interval extends from -0.883 to 0.483. The interval includes zero, so it does not isolate a single direction of difference. Its lower endpoint is compatible with fewer weekly episodes in the bupropion group, while its upper endpoint is compatible with more. The interval's width signals that the estimate is not highly precise relative to the range of possible differences it encompasses.

A confidence interval is not a guarantee that the true value lies within its specific endpoints, nor does it give the probability that the treatment effect is at any one value. In general, the interval is produced by a procedure with stated long-run coverage properties under its assumptions. Its interpretation depends on the design and analysis methods, some of which are not detailed in the registry record.

The secondary mean difference for percent BMI loss is 1.2, with a 95% confidence interval from -0.098 to 2.498. This interval also includes zero. It is compatible with a small difference in the opposite direction as well as with a larger positive difference. The posted interval therefore does not provide a sharply determined estimate for this secondary outcome.

Precision is distinct from whether a result meets a chosen threshold for statistical significance. The unadjusted p-values are 0.566 for the primary endpoint and 0.07 for the secondary endpoint. Neither should be interpreted without the effect estimate, its interval, the endpoint's role, and the limits of the registry's analysis details. The registry does not report a threshold for clinical importance, so the posted intervals cannot be used to classify effects as clinically meaningful or unimportant.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations give participants per arm, not total events. They are based on the observed effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning target is a stated fraction of the observed effect. For the primary endpoint, the rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The corresponding columns state the participants per arm for 80% power and participants per arm for 90% power.

In plain language, the 80% power column gives the planned group size for a study designed to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect is truly present and the assumptions hold. The 90% power column makes the analogous illustration for a 90% chance. These are planning targets, not a description of what happened in the completed trial. The listed requirements increase as the assumed effect becomes smaller, because a less pronounced difference is harder to distinguish from random variation.

For the primary endpoint, planning for 100% of the observed effect gives 722 participants per arm for 80% power and 966 participants per arm for 90% power. Planning for 75% gives 1,283 participants per arm for 80% power and 1,717 participants per arm for 90% power. Planning for 50% gives 2,886 participants per arm for 80% power and 3,863 participants per arm for 90% power.

These figures are illustrations calculated from the observed effect, not the trial's original design assumptions. The original sample-size justification is not reported in the registry record. This is not observed power: the completed study's result cannot be converted into a retrospective probability that the trial detected an effect.

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 = -0.200; pooled standard deviation σ = 1.356.
2. n = 2 × (1.96 + 0.842)² × 1.356² / -0.200² = 721.4, rounded up to 722 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 <- -0.2                      # observed difference in means
sigma <- 1.35577859299383                     # 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(414167)
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 = 722 (80% power), 966 (90% power)
 75% of observed effect: n per arm = 1,283 (80% power), 1,717 (90% power)
 50% of observed effect: n per arm = 2,886 (80% power), 3,863 (90% power)
power.t.test: 722.3 
Simulated power at n = 722 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and one listed secondary outcome. The primary outcome is frequency of binge eating episodes; the secondary outcome is percent BMI loss. The record does not report whether the trial specified a testing hierarchy, adjusted for multiple comparisons, or applied another procedure to control the risk of false-positive findings across outcomes. These details are not reported in the registry record.

Multiplicity matters because repeated statistical tests can produce an apparently notable result even when no underlying effect exists. This is a general property of multiple testing, not a claim that a posted result is false. Since the secondary comparison is labelled unadjusted and no adjustment is reported, it should be treated as exploratory or supportive rather than as an independent confirmatory conclusion. The primary endpoint remains the central comparison for the stated research question.

The registry's primary endpoint description specifies baseline forward imputation for missing data. It does not provide the number of missing observations, the reasons for missingness, the exact imputation implementation, or sensitivity analyses under alternative assumptions. The secondary outcome record does not give a missing-data method. The different posted group counts for the secondary result are not explained. These omissions limit assessment of how missing observations and analysis-set selection may have influenced the estimates.

The registry does not report whether analyses used an intention-to-treat population, a per-protocol population, or another defined set. It also does not report the protocol's statistical analysis plan, model selection, covariate adjustment, interim analyses, or handling of protocol deviations. Although outcome summaries and comparison estimates are posted, the registry lists zero reported analyses. This means the record does not provide a detailed account of the analytical decisions behind the results. The original sample-size assumptions and justification are also not reported.

These gaps do not invalidate the posted results, but they constrain how confidently their methods can be evaluated. They leave open questions about prespecification, robustness to missing data, and the intended interpretation of secondary analyses. They should not be filled by assumptions about usual practice.

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 0% reporting threshold.

The posted serious adverse event summaries list 31 participants at risk in the bupropion group and 30 in the placebo group. The recorded number affected by a serious adverse event is 0 in each group. The summaries also list 31 and 30 participants at risk for other adverse events, with 0 affected in each group.

These are registry-reported counts for the posted safety summaries. They do not establish that no adverse events occurred outside the reported categories, and they do not describe event types, timing, severity beyond the serious classification, or the method of collection. No serious adverse event terms are listed. Death counts are not reported in the registry record.

As a general statistical point, a count of zero in a study group does not prove that the underlying risk is zero. Safety estimates depend on the amount and duration of observation, the definition of events, and completeness of reporting. The registry record does not provide enough detail to assess those aspects fully. The posted figures should therefore be read as reported event counts, not as a guarantee about safety.

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

The primary posted result describes a mean difference of -0.2 episodes per week for bupropion relative to placebo at post treatment. The confidence interval, from -0.883 to 0.483, includes zero and spans differences in either direction. The unadjusted p-value is 0.566. Together, these statistics show that the estimate is uncertain and do not establish a clear between-group difference in the primary endpoint.

This does not prove that the treatments had identical effects. A confidence interval that includes zero can also include nonzero differences, and the interval's range should be considered when judging what the study can distinguish. Conversely, the point estimate alone should not be treated as proof of a benefit. The registry does not state a threshold for a clinically important difference, so the posted result cannot establish whether any values in the interval would matter clinically.

The secondary BMI-loss result is also uncertain: its confidence interval includes zero, and its unadjusted p-value is 0.07. Because it is a secondary outcome and no multiplicity procedure is reported, it should not be treated as definitive confirmation of the primary result. The registry does not report whether changes in this measure were associated with changes in binge eating frequency.

Randomization and double masking are design features intended to support a fair comparison and reduce some sources of bias. The record does not provide enough implementation detail to assess whether masking was maintained, how treatment adherence was handled, or how participant withdrawals affected the analysis. The primary description does identify baseline forward imputation for missing data, but the amount and pattern of missingness are not reported.

The results are limited to the registered trial and its described outcomes and timeframes. They do not establish longer-term effects, explain the mechanism of any observed difference, or support conclusions for populations whose characteristics are not described. The study summary's stated expectation is not a result. The posted estimates describe the data and their uncertainty; they are not medical advice or a recommendation about treatment.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between the direction of an estimate and the certainty around it. The primary mean difference is negative, indicating a lower observed group mean for bupropion, but its confidence interval extends across zero and its unadjusted p-value is 0.566. Reading only the point estimate would omit the uncertainty that is central to interpreting the comparison.

It also shows why a primary endpoint and a secondary outcome should not be treated as interchangeable. Frequency of binge eating episodes was the primary measure aligned with the stated research question. Percent BMI loss adds another outcome, but the registry does not report a multiplicity strategy, a testing hierarchy, or analyses relating the measures. The secondary result therefore has a different evidential role.

Missing-data handling is another important part of the record. The primary result specifies baseline forward imputation, while the record does not describe the amount of missingness or sensitivity analyses. The secondary group counts differ from those posted for the primary endpoint, without an explanation. These are examples of why outcome estimates need to be read alongside information about analysis populations and missing observations.

Finally, the sample-size illustrations show how planning requirements depend on the effect assumed for detection. Their values are based on observed effects and stated planning assumptions; they are not the original design rationale and do not describe observed power. The registry does not report the trial's own sample-size justification. Taken together, these features make the record useful for understanding uncertainty and reporting limits, rather than for reducing the findings to a simple positive-or-negative label.

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.

Several limitations specific to this trial are apparent from the registry record. The primary outcome is measured over one week at post treatment, and the record does not report follow-up results beyond that assessment. The primary endpoint description specifies baseline forward imputation for missing data, but the extent and pattern of missingness and the method's implementation are not detailed. The registry does not report sensitivity analyses that might show how alternative missing-data assumptions affect the comparison.

The secondary BMI-loss summary includes 20 participants in the placebo group, while the primary summary includes 30. The registry does not explain this difference. It would be inappropriate to infer whether it reflects missing observations, a different analysis set, or another reason. The record also does not report whether the optional behavioral weight loss treatment was taken up or how it was incorporated into outcome assessment.

Further details about eligibility criteria, participant characteristics, adherence, withdrawals, protocol deviations, and the analysis population are not reported in the registry record. The statistical analysis plan, original sample-size justification, multiplicity handling, and interim analyses are also not reported. This limits assessment of prespecification and the robustness of the posted estimates.

The posted summaries are aggregate statistics rather than individual-level data. They do not show the outcome distribution, participant-level changes, or associations between outcomes. The serious and other adverse event counts are posted as zero affected in each group, but the registry does not provide detailed event descriptions or observation and collection procedures. These limits affect interpretation of both efficacy outcomes and safety reporting.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Craving, Binge Eating and Obesity — NCT00414167.
• Registry record last updated 2020-04-03; status last verified 2020-04.
• Results first posted 2014-03-28.
• 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

The registry record describes a completed, randomized, double-masked, parallel-group trial sponsored by Yale University. It lists phase 2 and phase 3 and an enrollment of 61. The study compared bupropion with placebo in people described as having binge eating disorder and obesity.

The primary endpoint was frequency of binge eating episodes, measured as episodes per week over one week at post treatment. The posted mean difference was -0.2, with a 95% confidence interval from -0.883 to 0.483 and an unadjusted p-value of 0.566. The listed secondary outcome was percent BMI loss; its mean difference was 1.2, with a 95% confidence interval from -0.098 to 2.498 and an unadjusted p-value of 0.07.

The primary endpoint description specifies baseline forward imputation. The registry does not report the original sample-size rationale, detailed analysis plan, multiplicity procedure, or several details needed to assess missing data and analysis populations. The posted results should be interpreted with those reporting limits in mind.