Effectiveness of Florbetapir (18F) PET Imaging in Changing Patient Management and the Relationship Between Scan Status and Cognitive Decline: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effectiveness of Florbetapir (18F) PET Imaging in Changing Patient Management and the Relationship Between Scan Status and Cognitive Decline (NCT01703702), a randomized phase 4 study. The primary outcome is Clinical and Diagnostic Change in Patient Management.

2. Clinical Question

The registry describes a randomized comparison of two management-information conditions. Both groups received the imaging procedure; what differed was whether physicians could use its result during the period relevant to the primary endpoint. The endpoint was a change in management, rather than a direct measure of diagnostic accuracy or cognitive decline.

The study also examined changes in clinical diagnosis and diagnostic confidence, along with aspects of management and caregiver self-efficacy. The title and study description include an interest in the relationship between scan status and cognitive decline. Numerical cognitive-decline findings are not reported in the registry record summarized in the posted results, so the management comparison cannot answer that separate question.

3. Trial Design

The registry classifies this as a phase 4, randomized, parallel-group study. It was open label, with no masking recorded for the study overall; however, the control-group description specifies that physicians were blinded to PET results for 12 months. The study is described as multicenter and multicountry. It was sponsored by Avid Radiopharmaceuticals and is recorded as completed.

Enrollment was 641. In the primary endpoint analysis, the intervention group included 300 patients and the control group included 299. These endpoint counts reflect the stated analysis population, which included only patients with both baseline and follow-up values. The registry does not report the full participant flow or explain the difference between overall enrollment and these analysis counts.

The intervention group’s physicians had immediate access to the florbetapir (18F) PET scan results. The control group’s physicians were blinded to those results for 12 months. Thus, the trial compared the clinical consequences of access to scan information during follow-up. The primary endpoint timeframe was baseline and 3 months, within the control group’s period of blinding.

The registry lists a start date of 2012-10 and a primary completion date of 2015-04. It does not report the original sample-size justification, the planned allocation ratio, the planned statistical analysis details, or whether interim analyses were conducted. Those design details should not be inferred from the posted outcome data or from planning calculations based on the observed effect.

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: 641 patients enrolled in the study. 21 patients withdrew before receiving a florbetapir (F18) PET scan. 620 patients received florbetapir and comprise the Safety Population; 2 patients did not have a valid PET scan. Therefore; 618 patients were randomized to the intervention or control arms and comprise the Efficacy Population.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Analysis population for this endpoint only includes those patients with both a baseline and follow-up value.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Clinical and Diagnostic Change in Patient Management, measured over Baseline and 3 months.

The primary endpoint was Clinical and Diagnostic Change in Patient Management, measured as the percentage of patients with a change in management from baseline to 3 months. The registry defines the comparison as the percentage in the immediate-access group versus the percentage in the group whose physicians received results 12 months later. The analysis population for this endpoint included patients with both baseline and follow-up values.

This endpoint addresses whether scan information is associated with a change in clinicians’ management decisions. It is relevant to the study’s management question because the assigned difference between groups was whether physicians could access the scan result. It is not, by itself, a measure of whether a diagnosis was correct, whether management changes were beneficial, or whether patients’ cognitive decline differed. Those are distinct questions and require their own outcome data.

The posted results give 68.0% in the intervention group and 55.5% in the control group. The registry also reports an odds-ratio analysis and its confidence interval. A percentage describes how common the recorded management change was within each group; it does not explain which kinds of management changed or the reasons for each change. The registry lists more detailed management outcomes as secondary measures, but each requires separate interpretation.

7. Results Posted in the Registry

• Intervention: 68.0% (204/300) versus 55.5% (166/299) on control; risk difference 12.5 percentage points (95% CI 4.8 to 20.2), risk ratio 1.22 (1.08–1.39); unadjusted two-proportion z-test p = 0.002.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Patient's Clinical Diagnosis

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Intervention Scan/Diagnosis Discordant: 85.6% (95/111) versus 11.9% (13/109) on control; risk difference 73.7 percentage points (95% CI 64.7 to 82.6), risk ratio 7.18 (4.28–12.02); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Intervention Scan/Diagnosis Discordant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Diagnostic Confidence

• 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:
  • Intervention Scan/Diagnosis Concordant: mean 23.54 versus 2.85 on control; difference 20.69 (95% CI 17.53 to 23.85), standardized effect d = 1.32; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Intervention Scan/Diagnosis Concordant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Patient Management: Advice/Counseling

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Intervention: 64.7% (194/300) versus 58.9% (176/299) on control; risk difference 5.8 percentage points (95% CI -2.0 to 13.6), risk ratio 1.10 (0.97–1.25); unadjusted two-proportion z-test p = 0.144.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary findings cover changes in clinical diagnosis, diagnostic confidence, and advice or counseling. Their directions and apparent strength differ, and the endpoints do not all use the same scale or analysis population. The diagnosis result is limited to patients classified as scan/diagnosis discordant, while diagnostic confidence is presented for patients classified as scan/diagnosis concordant. Advice or counseling is reported in the intervention and control groups.

These outcomes offer related but distinct perspectives on the primary management result. A change in diagnosis or confidence may accompany changes in management, but none is interchangeable with the primary endpoint. The secondary findings therefore provide context about particular aspects of the clinical process rather than an independent confirmation that every kind of management changed in the same way.

The registry lists additional secondary measures, including caregiver self-efficacy and individual management categories. Their numerical findings are not reported in the registry record. It also lists a total of five secondary outcomes, while numerical results are available for only some of those measures in the posted results. No conclusion about unreported secondary outcomes can be drawn from the results that are present.

Unadjusted secondary p-values carry less weight when several outcomes are examined because the chance of obtaining at least one small p-value can increase across multiple tests. In general, multiplicity procedures account for a family of comparisons and can alter how evidence is judged. The registry does not report whether a multiplicity plan was prespecified or applied. The secondary results are therefore most appropriately treated as supporting or exploratory evidence, with attention to their populations, outcome definitions, intervals, and the lack of reported multiplicity handling.

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

• Change in Patient's Clinical Diagnosis
• Change in Diagnostic Confidence
• Change in Patient Management: Advice/Counseling
• Change in Caregiver Self-efficacy
• Change in Patient Management: Individual Categories

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a chi-squared analysis of the primary binary outcome using an odds ratio. It also permits a simple unadjusted recalculation from the posted group counts. These approaches express the contrast in different ways: the odds ratio compares odds, while the risk difference compares the proportions directly. Neither measure describes the clinical content or value of a management change.

In general, an odds ratio compares the odds of an outcome in one group with the odds in another. An odds ratio of 1 corresponds to equal odds; values greater than 1 indicate higher odds in the group named first in the comparison, and values below 1 indicate lower odds. The sponsor-reported primary odds ratio is 1.70. Because an odds ratio is not a percentage difference, it should not be read as saying that the percentage with a management change was higher by 70 percentage points.

The primary recalculation also expresses the contrast as a risk difference: 0.125, with a 95% confidence interval from 0.048 to 0.202. This is calculated from the posted event counts and group sizes without adjustment. In general, a risk difference subtracts one group’s event proportion from the other group’s event proportion. It is an absolute-scale contrast, unlike an odds ratio, which is a relative measure based on odds. The registry’s primary reported analysis is the chi-squared odds-ratio analysis; the recalculated risk difference is a supplementary unadjusted description.

In general, a confidence interval gives a range of values compatible with the data and the statistical method under its assumptions. Its width reflects precision: a narrower interval indicates less statistical uncertainty, while a wider interval indicates more. A 95% confidence interval is not a statement that there is a 95% probability that the particular interval contains the true value. The primary reported interval is for the odds ratio, and the recalculated interval is for the risk difference; these intervals cannot be compared as if they were on the same scale.

The reported p-value for the primary endpoint is 0.002. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of the effect. The posted p-value is an unadjusted result; the registry does not report a multiplicity adjustment for the secondary outcomes.

The change-in-diagnosis secondary result is also binary and is reported with a chi-squared odds ratio. Its population is specifically the scan/diagnosis-discordant groups. The diagnostic-confidence outcome is continuous and is reported as a least-squares mean difference using ANCOVA. ANCOVA is a regression-based method that can estimate a group contrast while accounting for covariates included in the model. The registry record does not state the full covariate specification, so the adjustment details cannot be reconstructed from the summary alone.

The posted diagnostic-confidence group summaries are least-squares means with standard errors. The registry’s ANCOVA estimate is 20.69, with a 95% confidence interval from 18.95 to 22.43 and p < 0.001. The unadjusted recalculation gives a mean difference of 20.69 and a confidence interval from 17.53 to 23.85. That recalculation approximates standard deviations from the reported standard errors and group sizes; it is not the same as the registry’s adjusted ANCOVA analysis. The registry’s reported analysis and its model-based interval describe the sponsor’s analysis, while the recalculation is a simplified comparison of posted summaries.

The advice/counseling outcome is binary and has a reported odds ratio of 1.28, with a 95% confidence interval from 0.92 to 1.78 and p = 0.144. In general, when a confidence interval for a relative effect includes 1, the data are compatible with no group difference as well as with effects in either direction within the interval. That does not establish that the groups are equivalent; it indicates that the estimate is not precise enough to rule out those possibilities at the interval level used.

Over-dispersion is a general concern when count or binary data vary more than a chosen model assumes; it can make standard errors too small if ignored. The primary and listed binary analyses are described as chi-squared analyses, and the registry does not report an over-dispersion assessment. No additional claim about over-dispersion can be made from these summaries. More generally, summaries alone cannot establish whether model assumptions or data-quality checks were met.

The randomized, parallel-group structure supports a comparison between assigned access conditions, but the available summaries do not show the full analysis plan, all analysis populations, or missing-data procedures. The primary analysis population is explicitly restricted to patients with both baseline and follow-up observations. Details about how missing values were handled, whether other populations were used, and whether outcomes were adjusted for baseline characteristics are not reported in the registry record, except for the stated ANCOVA method for diagnostic confidence.

11. Confidence Intervals and Precision

For the primary odds-ratio analysis, the registry reports 1.70 with a 95% confidence interval from 1.22 to 2.38. The interval is above 1, the value representing equal odds. The recalculated risk difference is 0.125, with a 95% confidence interval from 0.048 to 0.202; this interval is above zero, the no-difference value for a risk difference. The two intervals address the same group comparison on different scales.

In general, precision depends on the amount of information in the data and the variability of the outcome, as well as the analysis method. A confidence interval represents statistical uncertainty, not all possible sources of uncertainty. It does not account for limitations such as incomplete outcome ascertainment, measurement choices, or unreported analysis decisions.

The secondary estimates have different degrees of precision and refer to different populations and scales. For advice or counseling, the reported odds-ratio interval runs from 0.92 to 1.78, spanning the no-difference value of 1. For diagnostic confidence, the registry’s ANCOVA interval runs from 18.95 to 22.43. The clinical-diagnosis result has a wide relative-effect scale, with an odds-ratio interval from 20 to 96.12, and applies only to the discordant subgroup. These intervals should be read in the context of their outcome definitions and analysis populations, not as interchangeable measures.

Confidence intervals do not resolve whether an estimated management change was clinically meaningful or beneficial. The registry does not report a threshold for a meaningful change in management or diagnostic confidence. Precision around the numerical contrast and interpretation of the outcome’s importance are separate issues.

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 are expressed as participants per arm, not as total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The registry’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under the stated assumptions for a calculation targeting an 80% chance of detecting the specified effect if that effect were present. The 90% power column gives the corresponding per-arm number for a calculation targeting a 90% chance. These are planning targets, not descriptions of the probability that this completed trial detected an effect.

The illustrations consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For the primary endpoint, the corresponding figures are 237 and 317 participants per arm for 100% of the observed effect; 429 and 573 for 75%; and 977 and 1,307 for 50%, for 80% and 90% power respectively. Smaller effects need more participants to detect under these assumptions, which is why the displayed requirements rise as the effect fraction falls.

These are calculations based on the observed effect, not the trial’s original design calculations. They are not observed power. They do not establish what power the trial had under its actual design assumptions, which are not reported in the registry record.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.555; treatment proportion p₁ = 0.680; average p̄ = 0.618.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6873 = 1.3470.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6816 = 0.5736.
4. n = (1.3470 + 0.5736)² / (0.1248)² = 236.8, rounded up to 237 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
p0 <- 0.555183946488294                          # control proportion
p1 <- 0.68                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1703702)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 237 (80% power), 317 (90% power)
 75% of observed effect: n per arm = 429 (80% power), 573 (90% power)
 50% of observed effect: n per arm = 977 (80% power), 1,307 (90% power)
power.prop.test: 236.8 
Simulated power at n = 237 per arm: 0.804 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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

For the primary outcome, the registry reports a chi-squared odds ratio of 1.70, with a 95% confidence interval from 1.22 to 2.38 and p = 0.002. The simple unadjusted recalculation from the posted event counts gives an odds ratio of 1.703, with a 95% confidence interval from 1.22 to 2.375 and p = 0.002. The estimates and intervals agree to the displayed precision.

The recalculation also gives a risk difference of 0.125, with a 95% confidence interval from 0.048 to 0.202. This is an additional unadjusted expression of the binary contrast, not a result reported as the sponsor’s primary analysis. Its scale differs from the odds ratio, so the values should not be compared numerically as if they measured the same quantity.

For diagnostic confidence, the registry reports an ANCOVA least-squares mean difference of 20.69, with a 95% confidence interval from 18.95 to 22.43 and p < 0.001. The recalculation from the posted group summaries has the same mean difference, but its interval is 17.53 to 23.85. The recalculated interval uses an approximate unadjusted method; the registry’s ANCOVA result is model-based. The registry does not report the covariate details needed to reproduce that adjusted analysis from the summary.

The registry does not flag a discrepancy between the reported analyses and the recalculations. The recalculations are best read as simple checks using posted summary statistics, not replacements for the registry’s stated analyses.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified as a comparison of management change from baseline to 3 months, and the registry reports a chi-squared analysis. The record also lists secondary outcomes and multiple analyses. It does not report a complete statistical analysis plan, a hierarchy among secondary outcomes, or a prespecified multiplicity procedure. Consequently, the posted secondary p-values should not be read as if control of the overall false-positive rate were established.

In general, testing many outcomes creates more opportunities for apparently unusual results to occur by chance. Adjustments or a prespecified testing sequence can address that issue, but the registry record does not state that either was used. This does not invalidate the individual estimates; it affects how strongly multiple unadjusted findings can be interpreted collectively.

The primary endpoint analysis population includes only patients with both baseline and follow-up values. The registry does not report the number of patients excluded for missing either value, the reasons for missingness, or the method used to address missing data. It does not report whether an intention-to-treat analysis, a per-protocol analysis, or another analysis population was used for the primary comparison. The reported endpoint counts alone do not establish how missing observations were handled.

The registry records randomization, but does not provide a detailed account of allocation implementation or the handling of deviations from assigned conditions. Overall masking is recorded as none, while the control physicians were blinded to scan results for 12 months. The record does not explain whether outcome assessors were masked or how management changes were classified. Those details could matter for an endpoint that involves recorded clinical decisions.

The diagnostic-confidence analysis is identified as ANCOVA, but the covariates and model specification are not reported. Interim analyses, stopping rules, and the original sample-size justification are also not reported in the registry record. These omissions limit independent assessment of the full analysis strategy.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: subdural haematoma (0.2%), cerebral haemorrhage (0.2%).

The safety population includes 620 participants. The registry lists 2 affected for serious adverse events and 36 affected for other adverse events. The serious adverse event terms reported among the most frequent are subdural haematoma at 0.2% and cerebral haemorrhage at 0.2%.

These are overall safety counts, not a comparison by randomized group. The registry summary does not provide treatment-arm-specific counts, event timing, or information about whether events were judged related to the intervention. The listed serious-event terms should not be treated as a complete description of every serious event unless the registry record establishes that; the available summary identifies them as the top serious terms.

A death count is not reported in the registry record. The safety summary also does not provide enough detail to assess differences in risk between the groups. These counts describe reported events in the safety population and do not establish a comparative safety conclusion.

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

The primary result shows that a higher percentage of patients in the immediate-access group had a recorded management change from baseline to 3 months than in the control group. The reported odds ratio and its confidence interval are consistent with a group difference on the odds scale, and the unadjusted risk-difference recalculation gives an absolute-scale estimate with an interval above zero.

This finding concerns the management process under the study’s access conditions. It does not show that every management change was beneficial, appropriate, or sustained. Nor does it establish that the PET scan produced more accurate diagnoses, improved patient outcomes, or altered cognitive decline. Those questions require outcome definitions and results that are not contained in the primary management comparison.

The study compared immediate physician access to scan results with a period of physician blinding, while both groups received scans. Thus, the result should not be described as a comparison of scanning with no scanning. The control group’s 12-month blinding period also means the primary baseline-to-3-month comparison addresses access during an earlier follow-up interval, not the long-term effect of remaining blinded.

Interpretation is limited by incomplete reporting of missing-data handling, analysis populations beyond the primary endpoint definition, and the full statistical plan. The secondary results address selected dimensions of diagnosis, confidence, and management, but do not all concern the same population. The registry does not report numerical cognitive-decline findings, despite the study’s stated interest in that relationship.

In general, statistical evidence about a group contrast does not by itself determine clinical importance. The registry does not give a threshold for a meaningful management change or report the specific actions underlying the primary endpoint. The numerical findings support a comparison of recorded management changes, but broader claims about patient benefit or the value of particular decisions are not established by these data.

18. Why This Trial Matters Statistically

This trial is statistically informative because it separates access to imaging information from receipt of the imaging procedure: both groups received florbetapir (18F) PET scans, while physician access to results differed. That design makes the primary contrast directly relevant to whether scan information was associated with a change in recorded management during follow-up.

The primary outcome is binary and is reported both as an odds ratio and through an unadjusted risk-difference recalculation. Seeing the comparison on relative and absolute scales helps distinguish the odds-based summary from the difference in event proportions. The confidence intervals add information about precision that a p-value alone does not convey.

The study also illustrates why endpoint definition and analysis population matter. The primary result includes only patients with both baseline and follow-up values, while some secondary outcomes are restricted to scan/diagnosis-concordant or discordant groups. Those analyses can illuminate different parts of the clinical process, but they do not automatically generalize to the full randomized population.

Finally, the record makes clear that statistical conclusions depend on more than a significant primary comparison. Missing-data procedures, multiplicity planning, model details, and the clinical meaning of recorded changes affect how broadly results can be interpreted. The registry reports a management finding, while leaving important information about cognitive outcomes and the consequences of management changes unreported.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary analysis is restricted to patients with both baseline and follow-up values, but the registry does not report the number or characteristics of participants without complete measurements, or how their missing data were handled. The relationship between enrollment and the endpoint analysis counts therefore cannot be fully assessed from the registry summary.

The overall study is recorded as having no masking, although control physicians were blinded to scan results for 12 months. The record does not describe masking of outcome assessors, procedures for classifying management changes, or safeguards against differences in how those changes were recorded. Because the primary outcome concerns clinical management, these details would help assess possible measurement or ascertainment effects.

The primary endpoint counts whether management changed, but the registry summary does not identify the specific actions, their direction, or their clinical consequences. It therefore cannot distinguish a change that was useful from one that was neutral or unfavorable. The record does not report a threshold for a clinically meaningful change.

Several secondary results are subgroup-specific, and numerical results for all listed secondary measures are not reported. The registry also does not report multiplicity handling, detailed model covariates for the diagnostic-confidence ANCOVA, interim analyses, or the original sample-size justification. The observed-effect planning illustrations cannot fill in those design details.

The study description includes an interest in cognitive decline, but numerical results for that outcome are not reported in the registry record. Safety results are presented for the safety population without randomized-group comparisons, and the death count is not reported. These reporting limits constrain conclusions about cognitive outcomes and comparative safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effectiveness of Florbetapir (18F) PET Imaging in Changing Patient Management and the Relationship Between Scan Status and Cognitive Decline — NCT01703702.
• Registry record last updated 2016-08-17; status last verified 2016-07.
• Results first posted 2016-08-17.
• 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

NCT01703702 is a completed phase 4 randomized, parallel-group study sponsored by Avid Radiopharmaceuticals. It enrolled 641 participants and compared immediate physician access to florbetapir (18F) PET scan results with physician blinding to results for 12 months; both groups received scans.

The primary endpoint was the percentage with a management change from baseline to 3 months, among patients with both baseline and follow-up values. The posted result was 68.0% in the intervention group and 55.5% in the control group. The registry reports an odds ratio of 1.70, with a 95% confidence interval from 1.22 to 2.38 and p = 0.002.

The record also lists secondary measures related to diagnosis, diagnostic confidence, management, and caregiver self-efficacy. Numerical cognitive-decline findings, detailed missing-data procedures, multiplicity handling, and the original sample-size assumptions are not reported in the registry record.