Neural Response to Food Stimuli: fMRI Changes Following Cognitive Behavioral Therapy for Binge Eating Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Neural Response to Food Stimuli: fMRI Changes Following Cognitive Behavioral Therapy for Binge Eating Disorder (NCT03604172), a randomized na study. The primary outcome is Blood Oxygen Level-dependent (BOLD) Functional Magnetic Resonance Imaging (fMRI) Response to Food-specific Stop-signal Task.

2. Clinical Question

This is a question about a measured neural response and eating-related outcomes over the registered timeframe. It is not, by itself, a question about every possible effect of therapy or about longer-term outcomes. The posted results compare changes in the assigned groups; they do not establish what would happen in other populations or under different treatment conditions.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. The sponsor was the University of Pennsylvania. The listed conditions were binge eating disorder and overweight and obesity. The phase field is recorded as NA. The trial status is completed, with a start date of 2018-08-08 and a primary completion date of 2021-06-23.

Participants were assigned to cognitive behavioral therapy or a waitlist control. The therapy arm received a 16-week cognitive behavioral therapy intervention for binge eating disorder. The waitlist arm was scheduled for 16 weeks on the waitlist, followed by 16 weeks of cognitive behavioral therapy. This design creates a comparison of the groups over the initial 16-week period; the registry’s primary outcome timeframe is change from baseline to 16 weeks.

The registry lists an enrollment of 40. For the primary fMRI analysis, the posted arm sample sizes are 18.0 for cognitive behavioral therapy and 16.0 for waitlist control. The record explicitly says fewer participants had usable fMRI data than the overall trial. The secondary outcomes each have posted group sample sizes of 20.0 and 20.0. These differences matter when interpreting the estimates: they describe the participants with outcome data, not necessarily everyone enrolled or assigned.

The design information does not establish details beyond what the registry records. The original sample-size justification, planned interim analyses, and original statistical analysis plan are not reported in the registry record. Masking is listed as none; no further information about how outcome assessment or data processing was conducted is 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: Fewer participants had usable data for the fMRI analysis than the overall trial.

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 Blood Oxygen Level-dependent (BOLD) Functional Magnetic Resonance Imaging (fMRI) Response to Food-specific Stop-signal Task, measured over Change from baseline to 16 weeks.

The primary endpoint is change from baseline to 16 weeks in BOLD fMRI response to high-calorie food cues during a food-specific stop-signal task. The response is expressed as percent signal change. The registry defines the measured signal as the mean BOLD response across a combination of reward regions of interest: prefrontal cortex, orbitofrontal cortex, insula, ventral tegmental area, and ventral striatum.

In general, BOLD fMRI measures changes in the blood-oxygenation signal associated with neural activity. The endpoint therefore captures a task-related brain response, rather than a direct measure of eating behavior or a clinical diagnosis. The food-specific task provides the stimulus context for the measurement, while the selected regions define the neural signal being summarized. The endpoint uses the mean across the specified regions rather than reporting each region as a separate primary measure.

This endpoint was used to address the trial’s stated research purpose: assessing whether cognitive behavioral therapy is associated with a change in neural response to binge-eating stimuli. The registry also reports three secondary eating-related measures, which provide different kinds of outcome information. The posted fMRI analysis includes fewer participants than the overall trial, a limitation relevant to the precision and representativeness of this neural estimate.

7. Results Posted in the Registry

• Cognitive Behavioral Therapy: mean -0.40 versus -0.30 on control; difference -0.10 (95% CI -0.38 to 0.18), standardized effect d = -0.24; z-test p = 0.480.

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.

Binge Eating Episodes

• 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:
  • Cognitive Behavioral Therapy: mean -9.00 versus -4.00 on control; difference -5.00 (95% CI -10.54 to 0.54), standardized effect d = -0.56; z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cognitive Behavioral Therapy and the control. The interval gives the range of effects that remain compatible with the data.

Reward-based Eating Drive

• 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:
  • Cognitive Behavioral Therapy: mean -15.00 versus 3.00 on control; difference -18.00 (95% CI -26.32 to -9.68), standardized effect d = -1.34; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Cognitive Behavioral Therapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Dietary Disinhibition

• 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:
  • Cognitive Behavioral Therapy: mean -4.00 versus 0.00 on control; difference -4.00 (95% CI -6.77 to -1.23), standardized effect d = -0.89; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Cognitive Behavioral Therapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover different aspects of eating-related behavior: binge eating episodes, reward-based eating drive, and dietary disinhibition. They complement the neural endpoint by providing behavioral and scale-based measurements rather than a task-related fMRI response. Their estimates are not interchangeable with the primary outcome, because the measures have different units and capture different constructs.

The overall pattern is not uniform. The posted contrasts differ in their direction and precision, and the intervals do not all relate to zero in the same way. This makes the secondary findings useful as context for the trial’s broader set of measurements, but they do not convert the primary fMRI comparison into a more precise result. Nor do they establish that a change in a scale measure explains a change in neural response; the registry does not report an analysis linking these outcomes.

Each secondary comparison is unadjusted. When several outcomes are examined, the chance of finding an apparently notable result somewhere among them can be greater than when only one comparison is made. In general, multiplicity procedures address this issue by changing how evidence is evaluated across outcomes. A multiplicity adjustment is not reported in the registry record. Therefore, individual secondary p-values and intervals should be treated as exploratory context rather than as independent confirmatory conclusions.

The record lists the secondary outcomes and their 16-week timeframe, but it does not report a detailed plan specifying which outcomes were confirmatory, how they were prioritized, or how missing observations were handled. The secondary results can indicate areas for further study, while the absence of these details limits how strongly they can support claims beyond the registered comparisons. Their relationship to the primary result is contextual: they broaden the set of measured outcomes, but they do not directly validate the fMRI result or establish a mechanism.

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

• Binge Eating Episodes
• Reward-based Eating Drive
• Dietary Disinhibition

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome measures are continuous: the primary endpoint is a mean percent signal change, and the secondary outcomes are means on their stated scales. The registry reports group changes and standard errors, then provides unadjusted mean differences, confidence intervals, and p-values. A mean difference compares the average change in one arm with the average change in the other. In the posted comparisons, the contrast is cognitive behavioral therapy minus waitlist control. A negative contrast therefore indicates a lower numerical change in the cognitive behavioral therapy group than in the waitlist group; its substantive meaning depends on the measure and its scale.

What does a standard error describe?

In general, a standard error describes the uncertainty in an estimated mean. It reflects how precisely the group mean is estimated, rather than the full spread of individual observations. Standard errors can be used when estimating uncertainty around means and contrasts. They should not be mistaken for standard deviations or for a range containing most individual responses. For the primary outcome, the reported standard error is 0.1 in each arm. For the secondary outcomes, the group standard errors are also posted alongside each mean change.

How should a mean difference be read?

The mean difference condenses the comparison into one estimate on the outcome’s original scale. For the primary endpoint, the posted difference is -0.1 percent signal change. For binge eating episodes, the difference is -5.0 episodes in the past 28 days. For reward-based eating drive, it is -18.0 score units, and for dietary disinhibition it is -4.0 score units. These values are unadjusted comparisons of the posted summary statistics. They do not account for covariates unless an analysis explicitly says so; such an adjusted analysis is not reported in the registry record.

What does a confidence interval add?

In general, a confidence interval shows the range of estimates compatible with the data under the calculation method and its assumptions. It communicates uncertainty and direction more fully than a point estimate alone. An interval that includes zero means the data are compatible with no difference as well as with differences on either side of zero. An interval that excludes zero indicates that the corresponding unadjusted interval does not include no difference. Neither situation on its own establishes clinical importance, confirms a causal mechanism, or resolves problems such as multiple comparisons and missing observations.

The primary interval is -0.377 to 0.177. It includes zero and extends to both negative and positive differences. The primary unadjusted p-value is 0.48. A p-value measures how unusual results at least as incompatible with a specified no-difference model would be under that model and the test assumptions. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. The registry record does not report the trial’s original statistical analysis plan, so the posted p-value should not be assumed to reflect a fully specified confirmatory analysis.

Why do unadjusted recalculations need care?

The comparison calculations are unadjusted recalculations based on posted summary statistics. They provide a transparent way to describe the between-group estimates using the available means and standard errors. They are not a substitute for a sponsor’s reported analysis when one is available. No reported analyses are listed for the secondary outcomes, and the record gives zero reported analyses overall. The original model specification, covariate adjustments, missing-data procedure, and multiplicity approach are not reported in the registry record. The calculations should therefore be interpreted as descriptive statistical comparisons rather than assumed to reproduce an unpublished planned analysis.

In general, assumptions matter when deriving standard errors and intervals from summary information. A calculation based on group means and standard errors cannot recover participant-level information, assess unusual observations, or check whether a model’s assumptions hold. It also cannot show whether the estimate changes under alternative missing-data assumptions. The registry does not report distributions of individual change scores or a detailed account of usable scans beyond noting that fewer participants had usable fMRI data.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a statistical model expects. It can make standard errors too small if a model fails to account for the extra variation, leading to confidence intervals that are too narrow and tests that appear more decisive than the data warrant. This concept is particularly relevant to count outcomes when counts vary more widely than a simple model assumes. The registry reports binge eating episodes as a continuous mean outcome with standard errors, but does not report a count model or an over-dispersion assessment. It would not be justified to claim that over-dispersion was present or that a particular model addressed it.

Randomization supports a between-group comparison by assigning participants to intervention conditions, but it does not eliminate uncertainty or missing outcome data. No masking was recorded, and fewer participants had usable fMRI data than the overall trial. In general, missing outcomes can affect both precision and validity if the participants with observed data differ from those without usable measurements. The registry does not report how this issue was handled. The available summaries therefore describe the posted analysis groups and should not automatically be generalized to all enrolled participants.

11. Confidence Intervals and Precision

The primary mean difference is -0.1 percent signal change, with a 95% confidence interval from -0.377 to 0.177. The interval crosses zero and includes values on both sides of no difference. This means that the point estimate should not be treated as precise evidence for a direction of group difference. The interval is compatible with a lower mean change in the cognitive behavioral therapy group, a higher mean change, or a value near no difference, under the unadjusted calculation.

Precision is shaped by the amount and variability of information available. The primary fMRI analysis has 18.0 participants in the cognitive behavioral therapy arm and 16.0 in the waitlist arm, and the registry explicitly notes fewer usable fMRI observations than overall trial participants. The arm-level standard errors are both 0.1. These summaries help describe uncertainty in the means, but they do not reveal the distribution of individual measurements or the effects of any unreported missing-data method.

A confidence interval is not a guarantee that the true effect lies within its endpoints. In general, it is an interval procedure whose long-run coverage depends on the statistical method and assumptions. Nor does an interval that crosses zero prove that the groups are identical; it indicates that the estimate is uncertain at the displayed level of precision. Conversely, an interval excluding zero would not alone establish importance or answer questions about bias, selection, or multiplicity.

The secondary estimates have different degrees of precision, as reflected by their respective intervals. Their interpretation should account for the same distinction between a point estimate and the range of values compatible with the calculation. The registry record does not report a single prespecified approach for interpreting these intervals across the full set of outcomes, so the precision of each individual comparison should not be confused with certainty about the overall set of findings.

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 or total events. They are planning illustrations based on the observed effect, not the trial’s original design calculation. The listed 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 in turn to the stated fraction of the observed effect. The original sample-size assumptions for this trial are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design that would have an 80% chance of detecting the selected effect under the listed assumptions, if that effect and those assumptions were correct. The 90% power column uses a higher target chance of detection and generally requires more participants per arm. These are design-planning quantities, not estimates of what happened in this trial.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. This is because smaller differences are harder to distinguish from random variation when other assumptions remain the same. The observed effect is uncertain, so using it as the basis for a future planning illustration should not be treated as a guarantee that the same effect will recur. These values are not observed power; observed power is not a useful replacement for interpreting the estimate and its confidence interval after results are available.

The posted planning illustrations use the comparison-specific observed effects and should be read as conditional examples. They do not establish that the trial was designed around those effects, that the assumptions match the original protocol, or that the listed sample sizes would be adequate under other models, outcome definitions, or missing-data patterns. The trial’s actual primary fMRI analysis group sizes are separate from these planning figures.

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 = -0.100; pooled standard deviation σ = 0.413.
2. n = 2 × (1.96 + 0.842)² × 0.413² / -0.100² = 267.8, rounded up to 268 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 <- -0.1                      # observed difference in means
sigma <- 0.413067791046458                     # 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(3604172)
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 = 268 (80% power), 359 (90% power)
 75% of observed effect: n per arm = 477 (80% power), 638 (90% power)
 50% of observed effect: n per arm = 1,072 (80% power), 1,435 (90% power)
power.t.test: 268.8 
Simulated power at n = 268 per arm: 0.799 (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 lists one primary outcome and three secondary outcomes. It does not report a multiplicity adjustment, a hierarchy among the outcomes, or a complete statistical analysis plan. When multiple comparisons are examined, general statistical practice recognizes that isolated p-values can overstate the strength of evidence if the number of opportunities to obtain a small p-value is not considered. Without a reported plan, the secondary p-values should be read as unadjusted and interpreted cautiously. The record does not establish whether a multiplicity approach was planned or used outside the posted information.

The record lists zero reported analyses overall, and no reported analyses are listed for the secondary outcomes. The posted comparison values are unadjusted recalculations from the arm-level summary statistics. The original model, any covariate adjustment, the primary analysis population, and the handling of protocol deviations are not reported in the registry record. Consequently, it is not possible from the registered results to determine whether the posted summaries match a prespecified analysis in every respect.

Missing data are particularly relevant to the primary fMRI endpoint. The registry states that fewer participants had usable data for fMRI analysis than the overall trial. It gives primary-outcome analysis group sizes of 18.0 and 16.0. The record does not report why scans were unusable, whether missingness differed by group, or what assumptions or procedures were used to address missing outcomes. In general, if the availability of an outcome is related to participants’ characteristics or responses, an analysis restricted to observed data may not represent the full randomized groups.

The secondary outcomes have posted group sizes of 20.0 in each arm, but the registry does not report a missing-data method for those measures either. The analysis population is not identified as intention-to-treat, per-protocol, or another defined population. Those labels should not be inferred from the arm counts. Without a reported analysis population and missing-data strategy, the numerical estimates are informative descriptions of posted results, but their relationship to all randomized participants is uncertain.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry records zero serious adverse events among the 20 participants at risk in the cognitive behavioral therapy group and zero among the 20 participants at risk in the waitlist control group. Deaths are recorded as zero in both groups. Other adverse events are also recorded as zero in each group. No serious adverse-event terms are listed.

These figures describe the adverse-event entries in the registry record for the stated groups. A zero count means that no event of the relevant type was recorded in the posted results; it does not establish that no event occurred outside the reporting definitions, observation period, or data-collection process. The record does not provide further details about event definitions, ascertainment, severity grading beyond the serious-event category, or the timing of safety follow-up. The figures should therefore be read as registry reporting, not as a complete assessment of every possible harm.

The waitlist group was scheduled to receive cognitive behavioral therapy after the waitlist period. The posted adverse-event counts should be interpreted within the groups and reporting information recorded, rather than assumed to describe all later treatment exposure. The registry does not report additional safety analyses.

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

The primary result is an estimated between-group difference in change in fMRI response, accompanied by a confidence interval that includes zero. This describes uncertainty in the posted comparison; it does not demonstrate that the groups had exactly the same response, and it does not establish a clear difference. The estimate concerns the specified task, high-calorie food cues, reward-region combination, and 16-week timeframe. It should not be generalized to other neural tasks, brain regions, outcomes, or follow-up periods without supporting evidence.

The secondary outcomes add information about eating-related measures, but their unadjusted comparisons do not establish a single overall conclusion about treatment. Different measures can move in different numerical directions and can have different scales. Interpretation also depends on what each scale represents, its measurement properties, and whether a particular direction is considered favorable. Those scale properties are not described in detail in the registry record, so the numerical changes should not be turned into claims about clinical benefit.

In general, statistical significance and clinical importance are separate questions. A p-value or confidence interval addresses compatibility with a statistical model and does not by itself show whether a change matters to participants. The registry does not report a threshold for a clinically meaningful difference. Nor does it report analyses linking the fMRI measure to changes in eating behavior, so the neural result should not be taken as proof of a mechanism connecting therapy with behavioral change.

The randomized design supports a comparison between assigned groups, but the study was open-label and the primary outcome analysis had fewer usable fMRI observations than the overall trial. Missing-data handling, analysis populations, and multiplicity procedures are not reported in the registry record. These uncertainties limit the strength and scope of conclusions. The posted data are a set of estimates for the registered outcomes and timeframe, not medical advice or a basis for predicting an individual participant’s response.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a neural primary endpoint with behavioral secondary outcomes in a randomized comparison. The primary outcome is not a simple clinical event or symptom count; it is a continuous fMRI measure averaged across several specified reward-related regions during a food-specific task. That makes clarity about the task, regions, and outcome scale important when interpreting the estimate.

The result also illustrates why a point estimate should be read with its interval. The primary mean difference is small relative to the span of its confidence interval, and that interval includes values on both sides of zero. The data therefore do not support a precise directional conclusion from the posted fMRI comparison. Emphasizing only the point estimate or only the p-value would omit information about uncertainty.

The smaller usable fMRI analysis group is another important statistical feature. An outcome can be technically unavailable even when a participant is part of the overall trial, and the resulting analysis may have less precision than the trial enrollment suggests. The registry flags this issue but does not report the missing-data procedure or reasons for unusable scans. That makes the completeness of outcome data relevant to both precision and interpretation.

Finally, the set of secondary outcomes invites a distinction between supportive context and confirmatory evidence. Their results broaden the range of measured outcomes, but the registry does not report a multiplicity strategy or full analysis plan. This trial is therefore a useful example of how randomized design, outcome availability, confidence intervals, and multiple comparisons jointly shape interpretation. The numerical findings are most informative when those features are considered together rather than in isolation.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint depends on usable fMRI data, and the registry states that fewer participants had usable data for that analysis than the overall trial. The primary comparison therefore reflects the posted fMRI analysis groups, not the full enrollment. The reasons for unusable data, whether data availability differed between groups, and the approach to missing observations are not reported in the registry record. These omissions limit assessment of possible selection effects and how representative the fMRI estimates are.

The study was open-label, with masking listed as none. The registry does not describe whether outcome assessors or image-processing staff were masked, so no further masking arrangements can be assumed. The primary outcome involves a task and a combined set of reward regions, but the record does not report separate estimates for each region. As a result, the posted summary does not show whether the component regions had similar or different patterns.

The record does not report the original sample-size justification, statistical analysis plan, interim analyses, analysis populations, covariate adjustments, or missing-data methods. It also lists no reported analyses for the secondary outcomes. The displayed comparisons are unadjusted recalculations from posted summaries. The absence of these details makes it difficult to assess whether all analyses followed a prespecified plan or how alternative reasonable methods might affect the results.

The primary endpoint and secondary measures cover a limited set of outcomes over the registered 16-week period. Longer-term results are not reported in the registry record. The secondary outcomes are unadjusted and are not accompanied by a reported multiplicity approach. Finally, the registry’s descriptions do not establish thresholds for meaningful change or links between neural and behavioral outcomes. These constraints limit conclusions about durability, clinical importance, mechanisms, and broader generalizability.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Neural Response to Food Stimuli: fMRI Changes Following Cognitive Behavioral Therapy for Binge Eating Disorder — NCT03604172.
• Registry record last updated 2023-04-18; status last verified 2023-03.
• Results first posted 2023-04-18.
• 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

NCT03604172 is a completed randomized, open-label, parallel-group trial sponsored by the University of Pennsylvania. It compared a 16-week cognitive behavioral therapy intervention for binge eating disorder with a waitlist control scheduled to receive therapy after 16 weeks. The registered primary outcome was change from baseline to 16 weeks in BOLD fMRI response to high-calorie food cues during a food-specific stop-signal task.

The primary unadjusted mean difference was -0.1 percent signal change, with a 95% confidence interval from -0.377 to 0.177 and an unadjusted p-value of 0.48. The interval includes zero. The registry notes fewer usable fMRI observations than overall trial participants. Secondary outcomes covered binge eating episodes, reward-based eating drive, and dietary disinhibition. Their comparisons are unadjusted, and the registry record does not report a multiplicity adjustment, full analysis plan, or missing-data methods.