The Role of Altered Nutrient Partitioning in Food Reward: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Role of Altered Nutrient Partitioning in Food Reward (NCT05200845), a randomized na study. The primary outcome is Change in Preference- Liking.

2. Clinical Question

3. Trial Design

The registry record describes a completed, randomized, single-masked, crossover pilot study sponsored by Virginia Polytechnic Institute and State University. It lists enrollment as 20 and the study condition as overweight and obesity. The recorded start date is 2022-02-23, and the primary completion date is 2023-06-01. The phase is listed as NA.

A crossover design exposes participants to more than one condition in a planned sequence, allowing outcomes under different conditions to be compared within the study. The listed sequences vary the order of CS+ and CS− beverage exposure and, separately, the order of high-fat and high-carbohydrate test meals. The record identifies randomized allocation and single masking, but does not specify who was masked or provide enough detail to reconstruct the full sequence schedule. It also does not report a washout interval or period-specific analysis plan.

The CS+ was a flavored beverage containing 75 calories of sucrose. The CS− was a flavored beverage with sweetness matched by sucralose. Other listed procedures included test meals inside a metabolic chamber and an fMRI scan. These procedures fit the stated research interest in nutrient use, metabolic responses, and food reward, but the primary comparison posted is for change in liking between the beverage conditions.

The record calls the study a proof-of-concept pilot aimed at assessing feasibility and measuring reward response across a range of body mass index and metabolic health. It does not report detailed eligibility criteria, participant characteristics, recruitment flow, or the number completing each procedure. The registry record does not report the original sample-size justification or the statistical plan used to design the trial.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 16 of 20 participants were randomized. Of those not randomized, 3 did not meet inclusion criteria and 1 declined to participate.

Overall Study

Reasons for not completing this period:

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 Change in Preference- Liking, measured over Baseline and at 4 weeks.

The primary endpoint is change in preference—liking—of the flavors used in the intervention. Ratings were taken at baseline and at 4 weeks using the Generalized Labeled Magnitude Scale. Its anchors run from Most Disliked Sensation Imaginable to Most Liked Sensation Imaginable; the record describes a score range of 0-100. A higher score from baseline to post-intervention is defined in the record as an increase in liking.

This outcome addresses whether conditioning a flavor with sucrose, compared with a sweetness-matched sucralose beverage, is accompanied by a difference in reported liking. It measures a subjective response, rather than food intake, body weight, metabolic health, or a clinical outcome. That distinction matters: a change in a preference rating may be relevant to a proposed food-reward mechanism, but it does not by itself establish a change in eating behavior or health.

The registry reports the endpoint as a mean with standard deviation. The posted condition means are 6.5 for CS+ and 4.5 for CS−, with standard deviations of 10.7 and 13.0, respectively. The estimated mean difference for CS− compared with CS+ is -2.0 units. The confidence interval extends from -10.52 to 6.521, so the estimate is imprecise and includes values on either side of no difference. The record does not report a separate sponsor analysis of the primary endpoint.

7. Results Posted in the Registry

• Conditioned Stimulus - (CS-): mean 4.50 versus 6.50 on control; difference -2.00 (95% CI -10.52 to 6.52), standardized effect d = -0.17; z-test p = 0.645.

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.

Post-test Preference - Wanting

• 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:
  • Conditioned Stimulus - (CS-): mean 47.70 versus 50.60 on control; difference -2.90 (95% CI -63.85 to 58.05), standardized effect d = -0.03; z-test p = 0.926.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conditioned Stimulus - (CS-) and the control. The interval gives the range of effects that remain compatible with the data.

Change in Preference- Wanting

• 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:
  • Conditioned Stimulus - (CS-): mean 147.30 versus 187.40 on control; difference -40.10 (95% CI -144.96 to 64.76), standardized effect d = -0.27; z-test p = 0.454.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conditioned Stimulus - (CS-) and the control. The interval gives the range of effects that remain compatible with the data.

Blood Glucose Response to Beverages

• 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:
  • Conditioned Stimulus - (CS-): mean 37.90 versus 882.40 on control; difference -844.50 (95% CI -1,108 to -581.38), standardized effect d = -2.32; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Conditioned Stimulus - (CS-) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several kinds of response: wanting and preference ratings, brain response to beverages, substrate oxidation after test meals, blood glucose and insulin responses, and energy expenditure. The registry lists 10 secondary outcomes as posted, while the primary question concerns change in liking. Taken together, these measures explore different links in the proposed pathway from nutrient exposure and metabolism to reward-related responses; they are not interchangeable outcomes.

The posted secondary comparisons do not form a uniformly precise pattern. Some estimates are uncertain, while the glucose comparison is much more separated from zero than the primary liking comparison. That broad contrast makes clear why the primary result should not be treated as a summary of every biological measure, and why a result in one secondary measure cannot establish the proposed mechanism as a whole. The endpoint-specific estimates and intervals should be read on their own scales and in light of their measurement windows.

Secondary outcomes can provide useful exploratory context, especially in a pilot study, but they usually carry less confirmatory weight than a prespecified primary endpoint. Examining many outcomes creates more opportunities for apparently notable findings even when there is no underlying effect. The registry record does not report a multiplicity adjustment, a hierarchy among secondary endpoints, or sponsor-reported analyses. Consequently, unadjusted secondary p-values should not be treated as if each were the sole planned test.

The secondary measures also differ in units, timing, and variability. A large numerical contrast in one measure cannot be compared directly with a small contrast in another without considering each measure’s scale and purpose. Together they may help identify questions for future research, but the record does not document a unified analysis linking these outcomes or showing that a change in one mediates a change in another. The primary liking estimate remains uncertain, and secondary findings do not remove that uncertainty.

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

• Post-test Preference - Wanting
• Change in Preference- Wanting
• Change in Preference- Wanting
• Blood Oxygen Level-dependent (BOLD) Response to Beverages
• Substrate Oxidation Response to Test Meals
• Blood Glucose Response to Beverages
• Blood Insulin Response to Beverages
• Energy Expenditure in Response to Beverages

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric liking score, and the registry summarizes it using means and standard deviations. A mean describes the average score in a condition; a standard deviation describes how spread out individual scores are around that average. These summaries are useful for describing the observed data, but they do not show the full distribution or how each participant’s response changed across conditions.

What does the mean difference represent?

The comparison is expressed as the mean for CS− minus the mean for CS+. The posted estimate is -2.0 units. A negative value means the CS− mean is lower on the scale than the CS+ mean in this comparison. The sign is a direction convention, not a judgment about whether either condition is desirable. The estimate is not a percentage change, and it should be interpreted in the scale’s units.

A mean difference is an effect estimate: it expresses the size and direction of the contrast in the units of the outcome. It is more informative than a p-value alone because it shows what difference the data estimate. However, an estimate must be considered alongside its uncertainty. The registry record does not report a sponsor-selected threshold for a meaningful change in liking, so the clinical or behavioral importance of a difference cannot be determined from the estimate alone.

What does a confidence interval add?

A confidence interval gives a range of values that are reasonably compatible with the observed data under the statistical procedure used. In general, a 95% confidence interval describes the long-run coverage of the method across repeated use under its assumptions. It is not a guarantee that the true value lies in the particular interval, and it does not assign probabilities to individual values after the data have been observed. For this primary outcome, the interval runs from -10.52 to 6.521, indicating that the estimate is not precise enough to rule out differences in either direction.

Why does crossover structure matter?

In a crossover study, a participant may contribute observations under more than one condition. Those measurements can be correlated because they come from the same person. A paired analysis can use that relationship, while a calculation that treats condition summaries as unrelated may not. The registry record identifies the study as crossover, but does not describe the sponsor’s analysis model, within-participant covariance, period effects, carryover assessment, or sequence adjustment. Those details are important for judging whether the statistical analysis matches the design.

The condition-level summaries and unadjusted comparisons can still describe the direction and rough scale of the observed contrast. But without a reported crossover model, readers cannot verify how the dependence between repeated measurements was handled or whether the stated uncertainty reflects it. The posted comparison should therefore be treated as a summary-based estimate, rather than evidence that every design feature was incorporated in a sponsor analysis.

How should the p-value be understood?

The unadjusted p-value for the primary comparison is 0.645. In general, a p-value measures how unusual data at least as discrepant as those observed would be if a specified null model were correct and the analysis assumptions held. A larger p-value does not prove that the null model is true, establish that the conditions are equal, or measure the probability that the result happened by chance. It is one component of an interpretation that should also consider the estimate, confidence interval, design, and prespecified analysis plan.

Here, the interval includes zero and the p-value is not small under commonly used thresholds. Together, these indicate that the posted summary comparison does not provide precise evidence of a nonzero mean difference. They do not demonstrate equivalence or exclude effects that could matter. No equivalence margin, prespecified decision threshold, or sponsor-reported primary model is available in the registry record.

What can be learned from the standard deviations?

The standard deviations of 10.7 for CS+ and 13.0 for CS− show that participant ratings varied around their respective condition means. In general, greater variation makes a mean difference harder to estimate precisely when other design features are unchanged. But a standard deviation does not show how paired condition ratings vary together. In a crossover study, the within-participant correlation can be central to the standard error of the contrast, and that correlation is not reported.

The record gives outcome-specific counts of 15 for each primary condition. Those figures describe the observations represented in the posted summaries; the registry does not explain why they may differ from the enrollment figure or report a participant-flow account. The distinction between enrollment and the observations used for an endpoint is important: missing outcome data can affect precision and, depending on why data are absent, can also affect the interpretation of the estimate.

In general, over-dispersion means that data vary more than a statistical model expects. It can make uncertainty estimates too small if a model fails to account for that extra variability. The primary measure is summarized as a continuous outcome with a standard deviation, and the registry does not report an over-dispersion diagnostic or model-based assessment. This general issue is not evidence that over-dispersion occurred in this study; it illustrates why the model and diagnostics matter.

Finally, the registry record reports no sponsor analyses and does not describe the statistical analysis plan. It does not report covariate adjustment, handling of missing data, analysis populations, or multiplicity control. Those omissions limit the ability to assess whether the posted summary comparison matches the intended primary analysis. The numerical summaries remain useful as descriptive and exploratory evidence, but their scope should not be extended beyond what is documented.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate locates the underlying contrast. The primary mean difference is -2.0 units, and its 95% confidence interval extends from -10.52 to 6.521. The interval includes zero and spans both negative and positive values. Thus the data are compatible with a lower CS− mean, little or no difference, or a higher CS− mean. The point estimate alone does not resolve that uncertainty.

The interval is wide in relation to the point estimate, so the primary comparison does not pin down the size or direction of the difference closely. The posted standard deviations, 10.7 for CS+ and 13.0 for CS−, also indicate notable variation in ratings. Precision depends not only on outcome variability and the number of observations, but also on the analysis and, in a crossover study, the relationship between each participant’s measurements under the conditions.

The registry record does not report a sponsor analysis model, the within-participant correlation, or a prespecified margin for a meaningful difference. Those omissions matter when assessing whether the interval accurately reflects the crossover design and whether its range would be considered important. The confidence interval is not evidence that all values within it are equally likely, and it should not be read as an equivalence finding.

The unadjusted p-value of 0.645 is consistent with the interval’s inclusion of zero, but it does not replace the interval’s information about plausible effect sizes. The most defensible reading is that the posted primary comparison is uncertain: the estimate is modest, while the interval leaves room for effects in either direction. More precise evidence would require a well-specified analysis that accounts for the study design and outcomes.

12. Planning a Similar Trial: Sample Size

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

The sample-size planning illustrations translate the observed comparison into hypothetical future-study sizes. For these continuous comparisons, the figures are participants per arm, not total events. The registry record’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the trial’s own original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm indicated by the stated assumptions for an analysis to have an 80% chance of detecting the specified effect if that effect is real and the assumptions hold. The 90% power column makes the corresponding illustration for a 90% chance. Power is a property of a planned design under assumed conditions; it is not a measure of whether the present trial’s result is true.

Rows that use a smaller fraction of the observed effect require larger participant counts. Smaller differences are harder to distinguish from random variation, so a study generally needs more information to detect them at the same significance level and target power. For the primary liking comparison, the illustrations use 100%, 75%, and 50% of the observed effect, with the displayed participant counts increasing as the assumed effect becomes smaller.

These figures are not observed power. They are not a retrospective rating of the completed study, and they do not correct for the crossover design or replace a design-specific sample-size calculation. The planning assumptions specify equal allocation between two arms, whereas the trial is identified as a crossover study. The registry record does not report how its original design accounted for repeated measurements, sequence, missing data, or any multiplicity considerations. Use the planning values as conditional illustrations, not as evidence that the trial was adequately or inadequately sized.

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 = -2.000; pooled standard deviation σ = 11.906.
2. n = 2 × (1.96 + 0.842)² × 11.906² / -2.000² = 556.3, rounded up to 557 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 <- -2                      # observed difference in means
sigma <- 11.9056709176762                     # 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(5200845)
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 = 557 (80% power), 745 (90% power)
 75% of observed effect: n per arm = 989 (80% power), 1,324 (90% power)
 50% of observed effect: n per arm = 2,226 (80% power), 2,979 (90% power)
power.t.test: 557.2 
Simulated power at n = 557 per arm: 0.800 (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 10 secondary outcomes as posted. It does not report a statistical analysis plan describing how these outcomes were prioritized, whether a hierarchy was specified, or whether any adjustment for multiple comparisons was planned. When many outcomes are examined, the chance of at least one apparently unusual result can increase. In general, multiplicity methods or a prespecified testing sequence can help control that issue; no such approach is reported in the registry record.

The posted comparisons are described as unadjusted. That makes them useful for exploratory interpretation, but it means the p-values should not be read as multiplicity-controlled evidence. The record reports zero sponsor analyses, so there is no documented sponsor-reported model or analysis set against which to compare the summary calculations. The original statistical plan, including any interim analyses or stopping rules, is not reported in the registry record.

Missing-data handling is also not reported. The registry does not describe whether outcome observations were missing, why any data were absent, how missing values were handled, or whether sensitivity analyses were conducted. The primary outcome summaries list 15 observations in each condition, while enrollment is recorded as 20. These figures alone do not explain participant flow or establish why some enrolled participants may not appear in an outcome summary. No missingness mechanism should be inferred from the counts.

The analysis population is not reported in the registry record. It is therefore unclear whether the reported summaries represent all randomized participants, those who completed both conditions, or another defined group. In a crossover study, exclusions or incomplete periods can affect which within-person comparisons are available. The record also does not report whether the analysis addressed period, sequence, or carryover effects, or whether it used an intention-to-treat, per-protocol, or other population definition.

These omissions do not prove that the investigators failed to conduct analyses or checks; they mean those details are not reported in the registry record. They limit independent assessment of the analysis choices, the role of missing observations, and the confirmatory status of the secondary findings.

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 0% reporting threshold.

The registry reports serious adverse event counts of 0 in each listed group: CS+, CS−, high-fat test meal, and high-carbohydrate test meal. It also reports other adverse event counts of 0 in each of those groups, and deaths of 0. The corresponding numbers at risk are 15 for CS+, 16 for CS−, 12 for the high-fat meal, and 10 for the high-carbohydrate meal. These are group-specific entries and should not be added to infer a unique participant total in a crossover study.

A zero count means no events of the listed type were recorded for that group in the registry results. It does not establish that an event is impossible, that every possible event was assessed, or that the procedures have no safety concerns. Counts from a small pilot and limited exposure cannot characterize uncommon outcomes precisely. The registry record does not provide further event descriptions, severity information beyond the serious-event category, or an explanation of how adverse events were collected and attributed across crossover periods.

These figures describe the posted safety reporting; they are not a recommendation about whether any procedure is suitable for an individual.

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

The primary result is an estimate of the difference in mean change in liking between two conditioned beverage conditions. It is not a direct estimate of a change in food intake, body weight, metabolic health, or clinical status. The recorded endpoint is a subjective rating on a scale, assessed at baseline and at 4 weeks. Its value lies in addressing a narrow question about flavor liking after the conditioning intervention.

The observed mean difference is -2.0 units for CS− compared with CS+, but its confidence interval, -10.52 to 6.521, includes zero and values in either direction. This means the posted comparison does not precisely determine whether mean liking changed more under one condition or the other. It does not prove that the conditions are equivalent, nor does it show that conditioning has no effect. A decision about meaningfulness would require a prespecified threshold and an analysis suited to the crossover design, neither of which is reported in the registry record.

The study’s stated objective is broader than the primary endpoint. It concerns feasibility of measuring reward responses and the potential relationship between altered nutrient use and food reward. The registry also lists imaging, test meals, and metabolic outcomes. Those procedures may address complementary research questions, but the primary liking estimate by itself does not establish a biological mechanism or connect metabolic response to subsequent behavior.

The trial is described as a proof-of-concept pilot, and the registry record does not give the original sample-size rationale, full participant characteristics, sponsor analysis model, or missing-data approach. These limits make the posted estimates exploratory rather than definitive. The sample-size planning illustrations are conditional projections based on the observed effect, not evidence of the completed study’s power.

Accordingly, the result should be understood as a preliminary estimate with substantial uncertainty. It may help frame future research questions about measurement and flavor–nutrient conditioning, but it cannot support conclusions about treatment efficacy, clinical benefit, or individual decisions. The registry record does not report evidence sufficient to make those broader claims.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a randomized crossover design with outcomes spanning subjective preference, metabolic response, and brain imaging. A crossover can be efficient for comparing conditions because participants may serve as their own reference. That advantage depends on appropriate analysis of repeated observations, and the registry record does not describe how the sponsor handled within-participant dependence, period, sequence, or carryover.

The primary liking estimate demonstrates why effect size and uncertainty should be considered together. The point estimate is -2.0 units, but the confidence interval extends from -10.52 to 6.521. The data therefore leave meaningful uncertainty about both direction and magnitude. Reading only the point estimate or the p-value would conceal that uncertainty; reading the interval makes the limits of inference more visible.

The pilot setting makes estimation and feasibility important alongside formal hypothesis testing. Planning illustrations based on the observed effect can show how demanding future studies might be under stated assumptions, but those projections are sensitive to the effect chosen and do not substitute for design-specific planning. In particular, a crossover study requires assumptions about the correlation of repeated outcomes that are not reported in the registry record.

The secondary outcomes add breadth but also raise the importance of prespecification and multiplicity. Without a reported analysis hierarchy or adjustment plan, secondary comparisons are better regarded as exploratory clues than as a collection of independent confirmatory tests. The record’s lack of a sponsor-reported analysis plan also limits reproducibility and appraisal of how the posted summaries were obtained.

More generally, this study illustrates that a clear biological motivation does not remove the need for transparent design and analysis reporting. Information on sequence, missing data, outcome definitions, and analysis populations would help readers judge how far the results can be generalized. The primary estimate remains useful as a pilot observation, but its uncertainty and the unreported analytic details should remain central to interpretation.

18. Limitations

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

The registry describes the study as a crossover trial, but does not report the analysis model or how repeated measurements within participants were handled. It also does not document period or sequence effects, carryover assessment, or washout details. These omissions make it difficult to assess whether the comparison reflects the design’s within-participant structure.

Enrollment is recorded as 20, whereas the primary outcome summaries list 15 observations in each condition. The record does not explain participant flow, completion by condition, or the reasons outcome observations may be unavailable. It also does not state the analysis population or the method used to handle missing data. The outcome counts should not be interpreted as a complete account of participation.

The registry record does not report detailed baseline characteristics, including the body mass index distribution, despite describing an objective spanning the normal-to-obese range. This limits assessment of which participants the results represent. The primary outcome is a subjective liking rating, and no threshold for a meaningful change is reported. Consequently, the practical importance of the estimated difference is uncertain.

The record reports no sponsor analyses or statistical plan. It does not specify whether covariates were used, how secondary outcomes were prioritized, whether multiplicity was controlled, or whether interim analyses were planned. The study also includes several distinct procedures and secondary outcomes, but the registry does not report an integrated analysis connecting them.

Finally, this is described as a proof-of-concept pilot, and the primary confidence interval is broad. The findings are therefore limited in precision and should not be generalized beyond the measured outcomes and study context. These limitations do not establish that the underlying procedures or analyses were inadequate; they identify details that are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Role of Altered Nutrient Partitioning in Food Reward — NCT05200845.
• Registry record last updated 2025-09-08; status last verified 2025-08.
• Results first posted 2025-02-13.
• 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

NCT05200845 is a completed randomized, single-masked crossover pilot sponsored by Virginia Polytechnic Institute and State University. The registry records enrollment as 20 and lists overweight and obesity as the condition. The primary outcome is change in flavor liking from baseline to 4 weeks, comparing a sucrose-containing CS+ beverage with a sweetness-matched sucralose CS− beverage.

The posted primary mean difference for CS− compared with CS+ is -2.0 units, with a 95% confidence interval from -10.52 to 6.521 and an unadjusted p-value of 0.645. The interval includes zero and leaves uncertainty about the direction and size of the difference. The record also lists secondary preference, metabolic, and brain-response outcomes, along with zero reported serious adverse events in each listed group.

The registry record does not report sponsor analyses, the original sample-size rationale, a statistical plan, missing-data methods, or the analysis population. The primary finding is best treated as a preliminary estimate from a proof-of-concept study, not a definitive conclusion about food behavior or health.