Brain Amyloid and Vascular Effects of Eicosapentaenoic Acid: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Brain Amyloid and Vascular Effects of Eicosapentaenoic Acid (NCT02719327), a randomized phase 2, phase 3 study. The primary outcome is Regional Cerebral Blood Flow Using Arterial Spin-labeling MRI.

2. Clinical Question

3. Trial Design

This completed randomized trial compared icosapent ethyl with matching gel cap placebo in a parallel-group design. The registry lists the study as PHASE2 and PHASE3, with quadruple masking and enrollment of 131 participants. The sponsor was the VA Office of Research and Development. The study start date is 2017-06-08, and the primary completion date is 2023-09-29.

The registry describes the intended population as middle-aged, cognitively healthy Veterans with increased risk of Alzheimer’s disease. Participants were randomized in a 1:1 ratio to icosapent ethyl 4 g daily or placebo. The primary outcome was regional cerebral blood flow measured at the 18 month study visit. The analysis focused on the posterior cingulate gyrus, with blood flow averaged across the right and left sides.

The registry lists cognitive performance and cerebrospinal fluid biomarkers of Alzheimer’s disease as secondary outcomes. It reports three outcome measures and five analyses overall, while two secondary outcomes have posted results. The listed outcome summaries include continuous measures reported as means and standard deviations.

Enrollment is the total listed for the study; the numbers contributing to particular outcome summaries differ. For the primary outcome, the posted arm summaries include 54 participants assigned to icosapent ethyl and 60 assigned to placebo. Missing baseline imaging values affected inclusion in the primary analysis: 23 participants had values imputed from baseline, while 17 participants had no baseline values and could not be included. Additional details about the trial’s original sample-size justification, full statistical plan, interim analyses, and multiplicity approach are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis sample is intent-to-treat (ITT), ASL values were imputed from baseline values for 23 participants (n=14 IPE and n=9 placebo); 17 participants lacked baseline ASL values (n=9 IPE, n=8 placebo) and could not be included in analyses.

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 Regional Cerebral Blood Flow Using Arterial Spin-labeling MRI, measured over 18 month study visit.

The primary endpoint was regional cerebral blood flow in the posterior cingulate gyrus, measured with arterial spin-labeling MRI at the 18 month study visit. The registry describes the outcome as a mean measured in mL/g/min, with standard deviation as the measure of spread. Blood flow was averaged across the right and left posterior cingulate gyrus.

The registry says this anatomical region was chosen because it aligned with a statistical region of interest considered sensitive to changes in cerebral blood flow in cognitively unimpaired adults at risk for Alzheimer’s disease. In general, an imaging measure of blood flow provides a quantitative physiological outcome; it is not itself a diagnosis of Alzheimer’s disease. The endpoint therefore addresses a brain blood-flow measure rather than the onset of dementia or a direct clinical diagnosis.

The reported arm means were 55.7 for icosapent ethyl and 54.5 for placebo, with standard deviations of 14.6 and 14.1, respectively. These are descriptive summaries of the observed outcome values. They do not by themselves establish whether the groups differ beyond what could be expected from sampling variation. That inference depends on the estimated contrast, its uncertainty, and the analysis method.

The primary endpoint was one part of a broader study that also assessed cognitive performance and cerebrospinal fluid biomarkers. A difference in blood flow would not automatically imply a corresponding difference in cognition, biomarkers, or later disease incidence.

7. Results Posted in the Registry

• Icosapent Ethyl (IPE): mean 55.70 versus 54.50 on control; difference 1.20 (95% CI -4.08 to 6.48), standardized effect d = 0.08; z-test p = 0.656.

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.

Cognitive Performance

• 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:
  • Icosapent Ethyl (IPE): mean 0.46 versus 0.61 on control; difference -0.16 (95% CI -0.59 to 0.28), standardized effect d = -0.13; z-test p = 0.480.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Icosapent Ethyl (IPE) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists cognitive performance and cerebrospinal fluid biomarkers of Alzheimer’s disease as secondary outcomes, and posts results for two secondary outcomes. The available pattern is not a set of consistent, precise treatment differences across the study’s outcomes: the posted secondary cognitive analysis has an interval that includes zero, as does the primary cerebral blood-flow analysis. The registry record does not give enough information in the listed secondary outcome titles to characterize the biomarker results beyond their presence among the outcomes.

Secondary outcomes provide complementary information, but they address different measurements from the primary blood-flow endpoint. A result on cognition or a cerebrospinal fluid marker would not be interchangeable with a blood-flow result. Nor would a difference in one measure, by itself, establish an effect on Alzheimer’s disease diagnosis or clinical progression. The outcomes should be interpreted according to their own definitions and analysis methods.

General: secondary outcomes often help describe a trial more broadly, but they may be less persuasive as confirmatory evidence when many outcomes are tested. With multiple comparisons, the chance of at least one apparently notable result arising by chance can increase. Unadjusted secondary results do not account for that multiplicity. Their evidential weight also depends on whether they were prespecified and how they fit into the testing hierarchy; that information is not reported in the registry record.

Accordingly, the secondary outcomes can inform the overall pattern of measurement, but they should not be used to override the uncertainty in the primary result. The registry record does not report a multiplicity adjustment strategy or enough detail to evaluate the confirmatory status of each secondary analysis.

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

• Cerebrospinal Fluid (CSF) Biomarkers of Alzheimer's Disease
• Cognitive Performance

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is continuous: regional cerebral blood flow is summarized using a mean and standard deviation. A mean describes the central value of observed measurements, while a standard deviation describes how spread out measurements are around that mean. These summaries make it possible to describe each arm and to estimate a difference between arm means.

What does the mean difference describe?

The unadjusted re-calculation compares the posted mean for icosapent ethyl with the posted mean for placebo. Its estimate is 1.2 mL/g/min. This is a difference between group averages, not a statement that every participant experienced that change. An unadjusted comparison uses the available summary statistics without accounting for additional covariates in a regression model.

The registry also reports a linear regression analysis with a slope of -2.18. In general, regression estimates can depend on the model’s outcome definition, predictors, and coding. The registry record does not give enough detail to establish that the slope is directly comparable to the re-calculated difference between means. The distinction matters: two estimates can both describe a treatment comparison while using different models or estimands.

What does a confidence interval convey?

A 95% confidence interval gives a range of values compatible with the estimate under the assumptions of the analysis. In general, wider intervals indicate less precision and narrower intervals indicate greater precision. For the unadjusted re-calculation, the interval extends from -4.081 to 6.481. Because it crosses zero, the data do not exclude either a difference favoring one group or a difference favoring the other under this contrast. A confidence interval is not a probability statement that the true effect lies within the specific interval.

How should the p-value be read?

A p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It does not measure the probability that the null hypothesis is true, the size of an effect, or its clinical importance. The unadjusted re-calculation has p = 0.656; the registry’s reported regression has p = 0.17. These values belong to different analyses and should not be conflated.

General statistical interpretation also requires attention to the analysis plan and the data structure. The registry does not report the full original statistical plan, the original sample-size justification, or any interim analyses. It is therefore not possible to assess from the record whether all modeling decisions followed a prespecified plan or how the reported analysis handled all design features.

Why can over-dispersion matter?

General: over-dispersion occurs when observed variability is greater than a model assumes. If a model understates variability, standard errors can be too small and confidence intervals can be too narrow. For this continuous outcome, the posted arm standard deviations describe variation in the measured values. The registry does not identify an over-dispersion issue, and the record does not support a claim that one affected the analysis.

The primary analysis also involves missing measurements. Baseline values were used to impute arterial spin-labeling values for 23 participants; 17 participants with no baseline values could not be included. In general, imputation uses assumptions to fill in missing data, and the validity of those assumptions affects interpretation. The registry description does not provide enough detail to assess the imputation method or the consequences of excluding participants without baseline measurements.

Finally, the trial reports several outcomes and analyses. General: when many outcomes or comparisons are examined, the chance of finding a nominally notable result by chance can increase. Whether and how to adjust for multiple comparisons depends on the prespecified testing strategy. That strategy is not reported in the registry record. The secondary outcomes should consequently be interpreted cautiously, especially when considering unadjusted results.

11. Confidence Intervals and Precision

The unadjusted re-calculation for the primary outcome estimates a mean difference of 1.2 mL/g/min, with a 95% confidence interval from -4.081 to 6.481. The interval includes zero and covers values on both sides of it. This means the point estimate alone should not be read as a precise description of the treatment contrast: the compatible range is substantially broader than the single estimate.

In general, a confidence interval reflects both the estimate and the uncertainty associated with it. A narrow interval can support a more precise estimate, while a wide interval leaves greater uncertainty about the size and direction of the underlying difference. The primary interval does not establish equivalence. A formal equivalence conclusion would require a prespecified equivalence margin, which is not reported in the registry record.

The registry’s own regression analysis reports a slope of -2.18 and a 95% confidence interval from -5.36 to 0.99. That interval also includes zero. Because the reported regression slope and the re-calculated mean difference arise from different analyses, their estimates and intervals should not be combined as if they represented the same quantity.

The record does not report a threshold for a clinically important difference in regional cerebral blood flow. Thus, statistical precision can be described, but the importance of particular values within these intervals cannot be judged from the registry information alone. Missing imaging data are another source of uncertainty: some values were imputed from baseline, and participants without baseline values could not be included. The record does not quantify how those choices affect precision or the estimated contrast.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. Because the listed outcomes are continuous and the table is for participants per arm, each figure refers to the number needed in each treatment group, not the total across both groups and not a total number of events.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for an analysis with an 80% chance of detecting the assumed effect under those planning assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. These are prospective planning concepts: they describe a design’s ability to detect a specified effect, if that effect and the assumptions are appropriate.

The rows use different fractions of the observed effect. Planning for a smaller effect requires more participants per arm, because smaller differences are harder to distinguish from sampling variation. The displayed counts are not a claim about how many participants the completed trial needed or actually had in each endpoint analysis. They are not observed power.

The illustration is tied to the observed effect in this trial, which can itself be uncertain. It should therefore be treated as a way to understand how assumed effect size and target power affect planning, not as a definitive recommendation for another study. A future design would require its own scientific assumptions and design choices.

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 = 1.200; pooled standard deviation σ = 14.339.
2. n = 2 × (1.96 + 0.842)² × 14.339² / 1.200² = 2,241.3, rounded up to 2,242 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 <- 1.2                      # observed difference in means
sigma <- 14.3387804572076                     # 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(2719327)
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 = 2,242 (80% power), 3,001 (90% power)
 75% of observed effect: n per arm = 3,985 (80% power), 5,335 (90% power)
 50% of observed effect: n per arm = 8,966 (80% power), 12,002 (90% power)
power.t.test: 2242.3 
Simulated power at n = 2,242 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. Analyses Reported by the Sponsor

The registry reports the sponsor’s analysis as a linear regression with a slope of -2.18, a 95% confidence interval from -5.36 to 0.99, and p = 0.17. The unadjusted re-calculation from the posted arm means estimates a mean difference of 1.2 mL/g/min, with a 95% confidence interval from -4.081 to 6.481 and p = 0.656.

These are not identical analyses. The re-calculation is a simple unadjusted comparison based on posted summary statistics; the reported result comes from regression. Regression can account for features of the analysis that are not represented in a raw comparison of arm means. The registry record does not report enough model detail to explain fully why the slope differs from the unadjusted mean difference or to reproduce the regression.

No discrepancy is flagged between the posted result and the re-calculation. The two analyses should be reported with their methods attached, rather than selecting whichever estimate appears more favorable. The registry’s reported analysis is the trial’s own analysis; the re-calculation is a supplemental, unadjusted view of the posted summaries. Both intervals include zero, but neither result by itself establishes equivalence or resolves the uncertainty about the size of the difference.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes a primary outcome as well as secondary outcomes and multiple reported analyses. When several outcomes or comparisons are tested, general statistical theory indicates that the chance of obtaining at least one result that appears notable under a conventional threshold can increase. Methods for addressing this include prespecifying a hierarchy of tests or adjusting significance thresholds, but the appropriate approach depends on the trial’s analysis plan.

The multiplicity strategy is not reported in the registry record. It is therefore not possible to tell from the posted information whether the secondary analyses were adjusted, whether a hierarchy was used, or whether some results were intended to be exploratory. The unadjusted secondary findings should be read with this uncertainty in mind rather than treated as independent confirmation of the primary outcome.

The registry describes the primary analysis population as intent-to-treat and reports that 23 participants had arterial spin-labeling values imputed from baseline. It also says 17 participants lacked baseline arterial spin-labeling values and could not be included in analyses. These details mean the outcome analysis did not include every enrolled participant in the same way. The record does not report the imputation method, the assumptions underlying it, or sensitivity analyses that would show how alternative missing-data assumptions might affect the result.

In general, missingness can affect both the estimate and its precision, particularly if the availability of measurements is related to outcomes or treatment assignment. The registry information does not establish whether that occurred. The term intent-to-treat should therefore be read alongside the stated exclusions and imputation, rather than as proof that every randomized participant contributed an observed primary outcome.

The registry also does not report the original sample-size justification, interim analyses, or the complete statistical plan. Without those details, readers cannot evaluate the planned handling of multiplicity, missing data, and analysis populations against the final reported analyses.

16. 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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fall (3.2%), chest pain or tightness (1.6%), laparoscopic prostatectomy (1.6%), surgery (1.6%), aortic aneurysm (1.6%).

The posted safety summaries give the number at risk and the number affected by serious adverse events and other adverse events in each group. For serious adverse events, 9 of 63 participants in the icosapent ethyl group and 7 of 68 in the placebo group were affected. For other adverse events, the corresponding counts were 13 of 63 and 19 of 68. The registry reports 0 deaths in the icosapent ethyl group and 1 in the placebo group.

The registry also lists serious adverse-event terms, including Fall at 3.2% and Chest pain or tightness, Laparoscopic prostatectomy, Surgery, Aortic aneurysm, and Pneumothorax at 1.6% each. These terms describe reported events; the registry summaries do not establish that an event was caused by the assigned treatment.

These figures are descriptive counts, not a complete assessment of comparative safety. Differences in counts should not be interpreted as causal effects without considering the trial design, event definitions, follow-up, and statistical analysis. The record does not provide enough information to determine the relationship of individual events to treatment or to draw conclusions about rare events.

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

The primary result describes an uncertain comparison in regional cerebral blood flow at the 18 month study visit. The unadjusted re-calculation estimates a mean difference of 1.2 mL/g/min, but its 95% confidence interval ranges from -4.081 to 6.481. The interval includes zero and permits values in either direction. The registry’s regression analysis also has a confidence interval that includes zero. The posted data therefore do not provide a precise estimate of the primary group difference.

This does not establish that the treatments are equivalent. The registry does not report an equivalence margin or a threshold for a clinically important change in blood flow. A result that does not clearly distinguish groups can reflect uncertainty, and it should not be interpreted as proof that no difference exists.

The study was designed to evaluate brain blood flow, cerebrospinal fluid markers, and cognitive performance in cognitively healthy Veterans at increased risk of Alzheimer’s disease. The primary endpoint is an imaging measure, not a diagnosis of Alzheimer’s disease. Results on this endpoint cannot by themselves establish whether treatment delays disease onset, changes future risk, improves quality of life, or affects healthcare costs.

The registry’s brief summary describes the motivation for studying prevention or delay of Alzheimer’s disease, but those broader aims are not outcomes established by the posted primary result. The record does not provide evidence in the primary outcome analysis about later dementia incidence. Nor does a blood-flow measurement directly establish a cognitive benefit.

Interpretation is also limited by missing imaging measurements, including participants whose values were imputed from baseline and those who could not be included because baseline values were unavailable. The full statistical plan and missing-data sensitivity analyses are not reported. Overall, the result is best understood as an imprecise estimate for a specific imaging endpoint in this trial population, rather than a conclusion about treatment effects on Alzheimer’s disease itself.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should distinguish an observed estimate from the range of values compatible with the data. The primary unadjusted estimate is 1.2 mL/g/min, but its 95% confidence interval extends from -4.081 to 6.481. Reporting the point estimate without its interval would conceal substantial uncertainty about both the size and direction of the comparison.

It also illustrates why the analysis method matters. The registry reports a regression slope, while the re-calculation compares posted arm means. Those quantities are not necessarily identical. Readers need to know what was estimated and how before interpreting a treatment contrast, especially when the registry does not provide enough model detail to reconstruct the reported regression.

Outcome populations and missing data matter as well. The registry describes an intent-to-treat analysis but notes baseline-value imputation for some participants and exclusion of those without baseline imaging values. Such details affect how the analysis population should be understood and what assumptions underlie its results.

Finally, the trial includes several outcomes. A primary endpoint, secondary measures, and safety summaries answer different questions and should not be collapsed into one overall claim. The record does not report a multiplicity strategy, so unadjusted secondary findings warrant particular caution. Together, these features make the study a useful example of interpreting confidence intervals, model-based versus unadjusted estimates, missing outcome data, and multiple endpoints without overstating what the registry results establish.

19. Limitations

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

Several trial-specific limitations affect interpretation. The primary outcome is a regional imaging measure at the 18 month study visit, not a direct measure of Alzheimer’s disease diagnosis or later disease incidence. The registry’s stated rationale for selecting the posterior cingulate gyrus does not make the imaging outcome a substitute for cognitive or clinical outcomes.

Missing primary outcome data are important. The registry says arterial spin-labeling values were imputed from baseline for 23 participants, while 17 participants lacking baseline values could not be included. The record does not describe the imputation method, its assumptions, or sensitivity analyses. It is therefore not possible to assess how alternative missing-data approaches might affect the estimate.

The sponsor-reported regression analysis is not fully specified in the registry record. The posted summary does not give enough information to reproduce the model or determine exactly how its slope relates to the unadjusted difference between arm means. The original sample-size justification, interim analyses, and complete statistical plan are also not reported.

The record lists multiple outcomes and analyses, but does not report a multiplicity strategy. That limits assessment of the confirmatory status of secondary results. The registry also does not specify a clinically important threshold for the primary imaging outcome, so the practical importance of values within its confidence interval cannot be judged from these data alone.

Finally, the safety summaries are counts and event terms. They do not, on their own, establish whether events were caused by treatment or provide a complete comparative assessment of safety. These limitations constrain what can be concluded from the registry results without invalidating the descriptive information that is posted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Brain Amyloid and Vascular Effects of Eicosapentaenoic Acid — NCT02719327.
• Registry record last updated 2024-11-26; status last verified 2024-10.
• Results first posted 2024-11-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02719327, titled Brain Amyloid and Vascular Effects of Eicosapentaenoic Acid, is listed as a completed PHASE2 and PHASE3 randomized, quadruple-masked, parallel-group trial with 131 participants. The sponsor was the VA Office of Research and Development. The study compared icosapent ethyl 4 g daily with matching gel cap placebo in cognitively healthy Veterans described as having increased risk of Alzheimer’s disease.

The primary outcome was posterior cingulate gyrus cerebral blood flow measured by arterial spin-labeling MRI at the 18 month study visit. The posted arm means were 55.7 for icosapent ethyl and 54.5 for placebo. The unadjusted re-calculation estimates a mean difference of 1.2, with a 95% confidence interval from -4.081 to 6.481. The registry’s regression analysis reports a slope of -2.18, a 95% confidence interval from -5.36 to 0.99, and p = 0.17.

The registry also lists cognitive performance and cerebrospinal fluid biomarkers as secondary outcomes. Missing imaging data, unreported details of the statistical plan, and the absence of a reported multiplicity strategy limit interpretation of the analyses. The primary result is an imprecise comparison of an imaging measure, not evidence by itself about Alzheimer’s disease diagnosis or onset.