Molecular and Functional PET-fMRI Measures of Analgesia in Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Molecular and Functional PET-fMRI Measures of Analgesia in Migraine (NCT01970943), a randomized na study. The primary outcome is Visual Analogue Scale (VAS) 0-10 Pain Rating.

2. Clinical Question

The central statistical question is whether pain ratings and imaging measurements differed between the placebo and no-intervention conditions in this study. The registry describes the broader scientific aim as comparing placebo response and related opioid release in migraine patients with healthy controls. However, the posted outcome summaries combine the groups rather than showing group-specific estimates or an interaction between health status and condition. Therefore, those summaries do not directly quantify whether the condition contrast differed between participants with migraine and healthy participants.

The study also reports pain anticipation and pain stimulation fMRI BOLD signals and PET diprenorphine as secondary outcomes. These measures offer related but distinct views of brain response and receptor-related signal. They should be read as additional exploratory or supportive evidence, not as interchangeable measures of the pain rating itself. The registry record does not report a detailed clinical question for each imaging measure beyond its named outcome and measurement unit.

3. Trial Design

This was a completed, randomized, single-masked crossover study registered as NCT01970943. The registry lists an enrollment of 23 and identifies the study conditions as migraine and healthy. The listed study dates run from 2012-09-01 to primary completion on 2014-04-30. The phase is listed as NA. Massachusetts General Hospital is named as the sponsor.

The two conditions were no intervention and saline injection (placebo). Both descriptions refer to PET-fMRI investigation in healthy subjects and patients with migraine; the no-intervention condition specifies no drug condition, while the placebo condition specifies a placebo condition. A crossover design means the comparison is organized around participants experiencing conditions within the study rather than assigning every participant to only one condition. The registry does not report the order sequence, washout interval, or detailed randomization procedure, so those design features cannot be described further.

Single masking is recorded, but the registry does not identify which people involved in the study were masked or explain how masking was maintained. It also does not report the allocation ratio or the method used to generate the randomized sequence. These omissions matter when assessing possible expectation effects, especially in a placebo study, but they do not establish that masking or allocation was inadequate.

The posted primary outcome is the mean Visual Analogue Scale pain rating on a 0–10 scale, with a timeframe of 1 day. The registry also lists three secondary outcomes: pain anticipation fMRI BOLD signal, pain stimulation fMRI BOLD signal, and PET diprenorphine. The participant counts shown for the two primary-condition summaries are 23 in each condition. Because this is a crossover study, those condition counts should not be interpreted as separate, independent groups of participants. The registry record does not report a participant flow account, exclusions, or the number contributing to each individual outcome beyond the posted arm summaries.

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: The study design was indeed crossover, but the cross-over was done immediately on the same day. In other words, participants were either scheduled to receive no intervention, and then placed placebo approximately 2 hours later to allow for washout. Or placed placebo first, and then no intervention approximately 2 hours later. No actual drug used.

Overall Study

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.

Population: healthy subjects and patients with migraine

6. Primary Endpoint

The registry lists the primary outcome as Visual Analogue Scale (VAS) 0-10 Pain Rating, measured over 1 day.

The primary endpoint is the Visual Analogue Scale (VAS) pain rating, reported as a mean on a 0–10 scale. The registry description says the scale runs from 0 for no pain to 10 for the most intense pain possible. Participants marked their pain level in response to contact heat used to induce experimental pain. The stated timeframe is 1 day.

A pain rating is a direct report of perceived intensity. It is useful in this study because the stated objective is to investigate whether placebo may reduce experimental pain, and the outcome captures the participant’s reported experience rather than an imaging signal. The scale is continuous in the registry’s statistical classification, and the posted summaries therefore use means and standard deviations.

The record says the primary outcome data are reported for the placebo condition, but the posted results include both placebo and no-intervention summaries. The mean rating was 7.2 in the placebo condition and 4.3 in the no-intervention condition. The reported contrast is no intervention minus placebo, so its negative direction corresponds to a lower mean rating in the no-intervention condition. This observed direction is not the same as the study description’s stated expectation that placebo may reduce pain. The posted numbers describe the recorded condition summaries; they do not explain the discrepancy in direction or establish why it occurred.

The registry does not report details such as the exact heat-stimulus protocol, the number of ratings taken, or whether the primary analysis adjusted for participant-level pairing. Those details would help clarify how the reported mean represents the pain response.

7. Results Posted in the Registry

• No Intervention: mean 4.30 versus 7.20 on control; difference -2.90 (95% CI -4.41 to -1.39), standardized effect d = -1.11; z-test p = <0.001.

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.

Pain Anticipation fMRI BOLD Signal

• 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:
  • No Intervention: mean 0.57 versus 1.17 on control; difference -0.61 (95% CI -1.09 to -0.12), standardized effect d = -0.73; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for No Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Pain Stimulation fMRI BOLD Signal

• 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:
  • No Intervention: mean 0.57 versus 1.15 on control; difference -0.58 (95% CI -1.06 to -0.10), standardized effect d = -0.70; z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for No Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

PET Diprenorphine

• 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:
  • No Intervention: mean 1.25 versus 1.21 on control; difference 0.04 (95% CI -0.09 to 0.16), standardized effect d = 0.17; z-test p = 0.570.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the two fMRI BOLD measures show contrasts in the same direction as the primary pain-rating contrast: the posted no-intervention means are lower than the placebo means. The PET diprenorphine outcome does not show a similarly clear separation in its posted summaries. This broad pattern suggests that the fMRI measures and pain rating move in a related direction in these aggregate comparisons, whereas the PET measure is less clearly differentiated.

These outcomes do not measure the same thing. The pain rating is a subjective intensity scale, the BOLD measures are imaging signals in arbitrary units, and PET diprenorphine is reported as a standard uptake value. A directionally similar contrast across outcomes does not establish that one measure caused another, nor does it validate a proposed biological mechanism. The posted results also do not show whether the patterns differ between migraine and healthy participants, despite that comparison being part of the study’s stated scientific aim.

Secondary results carry less weight when they are unadjusted and multiple outcomes have been examined. If many tests are considered, some may appear notable by chance even when there is no corresponding underlying effect. The registry record does not report a multiplicity correction, a prespecified hierarchy among secondary outcomes, or a complete analysis plan specifying which contrasts were confirmatory. The secondary findings should therefore be treated as supportive or hypothesis-generating rather than as independent confirmation of the primary result.

The posted secondary analysis information is also uneven. The record includes reported analyses for pain anticipation fMRI BOLD signal and PET diprenorphine, but no reported analysis entry for pain stimulation fMRI BOLD signal. The record does not explain why reporting differs across these outcomes. This makes it especially important to distinguish the descriptive summary-statistic comparisons from sponsor-reported tests and to avoid reading the set as a single, fully specified inferential analysis.

Overall, the secondary outcomes offer context about imaging measurements collected alongside the pain ratings, but they do not resolve the primary result’s direction, the migraine-versus-healthy comparison, or the limitations of the crossover analysis details.

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

• Pain Anticipation fMRI BOLD Signal
• Pain Stimulation fMRI BOLD Signal
• PET Diprenorphine

9. Statistical Interpretation

10. Statistical Methods Explained

The registry classifies the primary outcome as continuous and reports means with standard deviations. A mean describes the central value of the recorded ratings, while a standard deviation describes how dispersed participant measurements are around that mean. A mean difference expresses the contrast between two condition means. The posted primary estimate is defined as no intervention minus placebo, so a negative estimate means the no-intervention mean is lower.

What does a confidence interval represent?

A confidence interval gives a range of values compatible with the observed data under the calculation’s assumptions. It conveys uncertainty about the estimated contrast, not the range of individual participant ratings and not the probability that a particular treatment effect is true. For the primary contrast, the interval runs from -4.407 to -1.393. Its location on the negative side of zero is consistent with a lower mean in the no-intervention condition. The interval’s width also matters: it shows that the estimate is not known with unlimited precision.

How should the crossover design affect the reading?

In a crossover study, participants experience more than one condition, and each participant can contribute information to the within-person comparison. A paired analysis can account for the fact that measurements from the same person may be correlated. The registry identifies this study as crossover but does not report the participant-level differences, their standard deviation, or the within-person correlation. The simple recalculations based on posted summary statistics therefore cannot reconstruct a paired analysis. They should not be mistaken for the sponsor’s original model unless the registry explicitly reports that method for the outcome.

The recalculated comparisons use unadjusted summary-statistic calculations. The primary contrast has a recalculated mean difference and confidence interval, but the registry record does not post a corresponding sponsor-reported primary test in the analysis detail available for this endpoint. This does not establish that the sponsor did not conduct an analysis; it means that the specific primary analysis details are not reported in the registry record. For secondary outcomes, the record includes some reported t-tests, but those entries do not supply confidence intervals. The reported fMRI anticipation test lists a p-value of 0.05, while the recalculated unadjusted p-value is 0.014. The PET entry reports a p-value of .05, whereas its recalculated unadjusted p-value is 0.57. Differences between reported analysis fields and recalculated summaries should be read in light of their potentially different methods and reporting conventions, not resolved by assuming they are the same analysis.

Why can over-dispersion matter?

For a continuous outcome, variability is reflected in the standard deviation. When measurements vary substantially, the estimate of a mean difference is generally less precise than it would be with less variability, all else equal. Here, the posted standard deviations describe variation in each condition, but they do not reveal the distribution’s shape or whether a small number of observations strongly influence the mean. Over-dispersion is often discussed for count outcomes when variability exceeds a model’s assumed level; this trial’s primary outcome is continuous, so that specific count-data issue is not the central modeling concern. The more directly relevant unknowns include the paired variability and the assumptions used for the crossover comparison.

The standardized effect-size values in the recalculated summaries express the mean contrast relative to a pooled standard deviation. Such standardization can aid comparisons across measures, but it does not change the outcome’s original units or establish clinical importance. In a crossover setting, a standardized effect based on marginal group summaries may not match a paired standardized effect.

What does an unadjusted p-value tell us?

An unadjusted p-value evaluates how compatible the observed data are with a null hypothesis under the assumed statistical procedure. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. A small p-value can coexist with uncertainty about generalizability, bias, or model fit. Because several secondary outcomes are posted, interpreting each unadjusted test as if it were the only test can overstate the strength of the overall evidence. The registry record does not report a multiplicity adjustment.

The study’s stated biological aim includes opioid release and receptor availability, while the posted imaging outcomes include BOLD signals and PET diprenorphine. These are measurement outcomes, not direct proof of a mechanism. Statistical differences or a lack of detected differences in those measures cannot by themselves establish a causal pathway. The registry record does not report a detailed imaging analysis pipeline, region-of-interest approach, or adjustment strategy.

In short, the reported means and standard deviations allow descriptive comparison, and the recalculated estimates provide an unadjusted statistical reading of the posted summaries. The crossover structure, missing paired-data details, and absent full analysis plan limit how closely those calculations can represent the trial’s intended analysis. The registry record does not report the original sample-size justification, interim analyses, or a full statistical analysis plan.

11. Confidence Intervals and Precision

The primary mean difference is -2.9, with a 95% confidence interval from -4.407 to -1.393. Because the interval lies below zero, the posted comparison is consistent with a lower average rating in the no-intervention condition than in the placebo condition. The interval also indicates meaningful uncertainty about the size of that contrast: the data are compatible with effects across the range of values in the interval, subject to the calculation’s assumptions.

The confidence interval is based on a simple recalculation from posted summary statistics, rather than a reported participant-level paired estimate. Since the design is crossover, an analysis using within-person differences could have different precision. The registry record does not report the paired variance or correlation needed to reconstruct that estimate. Thus, the interval is useful as a summary-statistic comparison, but it should not be treated as a complete account of the sponsor’s intended crossover analysis.

Precision is also distinct from practical importance. The interval describes uncertainty in the average contrast, not whether a particular difference is meaningful to participants. The registry record does not define a threshold for clinical importance on the VAS, nor does it provide enough detail to assess how the observed contrast relates to such a threshold.

For the secondary outcomes, the confidence intervals and standard errors vary in width and should be read on each measure’s own scale. In particular, an interval spanning zero indicates that the posted estimate is compatible with no difference under the calculation; it does not prove the conditions are equivalent. Conversely, an interval excluding zero does not resolve concerns about multiple testing, crossover analysis, or generalizability. The record does not report adjusted intervals for the set of secondary comparisons.

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 derived from the observed effect, not the trial’s original design calculation. For these continuous outcomes, the figures are participants per arm, not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets the stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column gives the illustrative number of participants per arm under those assumptions for a design intended to have an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column uses a higher target chance of detection under the same planning framework. These are planning concepts, not guarantees: actual power and precision depend on the true effect, variability, analysis, and study conduct.

Each row represents planning for a different fraction of the observed effect. Planning for a smaller effect requires more participants because smaller differences are harder to distinguish from random variation. The figures should be viewed as scenario comparisons, not as evidence that the completed study had a particular probability of detecting its result. This is not observed power.

The illustrations assume equal allocation between two arms, while the trial is described as a randomized crossover study. The registry record does not report a sample-size calculation based on paired differences or explain whether the posted planning illustrations account for the crossover design. They therefore serve as general planning references rather than a reconstruction of the study’s original 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 = -2.900; pooled standard deviation σ = 2.608.
2. n = 2 × (1.96 + 0.842)² × 2.608² / -2.900² = 12.7, rounded up to 13 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 <- -2.9                      # observed difference in means
sigma <- 2.60768096208106                     # 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(1970943)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 23 (80% power), 31 (90% power)
 50% of observed effect: n per arm = 51 (80% power), 68 (90% power)
power.t.test: 13.7 
Simulated power at n = 13 per arm: 0.776 (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 record lists a primary outcome and three secondary outcomes, but it does not report a plan for controlling multiplicity across these measures. When several outcomes or contrasts are tested, the chance of at least one apparently notable result can increase. An adjustment or a prespecified testing hierarchy can address that issue, but neither is described in the registry record. Consequently, the unadjusted secondary p-values should not be interpreted as if each were the sole planned test.

The record does not report how missing outcome data were handled, whether any participants were excluded from particular analyses, or whether analyses followed an intention-to-treat or another defined population. It also does not provide a participant flow account or outcome-specific counts beyond the posted condition summaries. These omissions make it difficult to assess whether missingness or exclusions could have influenced the estimates.

For a crossover study, it would also be useful to know whether the analysis accounted for condition order, period effects, carryover, and within-participant correlation. The registry identifies randomization and crossover, but the relevant details and model are not reported. Without them, the recalculated comparisons from marginal means and standard deviations cannot establish whether those design features were handled in the sponsor’s analysis.

The registry record does not report interim analyses, the original statistical analysis plan, or whether the outcome and analysis choices were finalized before results were examined. Their absence from the record does not show that these procedures did not exist; it means their role cannot be evaluated from the posted information. These reporting gaps are important when interpreting multiple outcomes and distinguishing confirmatory findings from exploratory analyses.

15. Safety Results

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

Other (non-serious) adverse events

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

The adverse-event summary reports zero serious adverse events in the no-intervention condition and zero in the placebo condition. It also reports zero other adverse events in each condition. The number at risk is listed as 23 for each condition. These are the registry’s posted counts for the recorded groups and do not by themselves establish that no unrecorded events occurred.

The registry record does not list serious adverse-event terms and does not provide death counts. It also does not describe the method or period used for adverse-event collection beyond the study outcome timeframe information elsewhere in the record. Therefore, the safety summary is limited to the event counts posted; it cannot characterize event severity beyond the serious-versus-other categories, timing, or any causal attribution.

Because this is a crossover study, condition-specific counts should be read in the context of participants experiencing study conditions, not as independent parallel groups. The record does not explain how an event occurring across periods was assigned to a condition or how repeated exposure was handled. These figures are descriptive registry entries and should not be expanded into broader claims about safety.

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

The posted primary data show different mean pain ratings in the two conditions, with a lower average in the no-intervention condition than in the placebo condition. The unadjusted comparison is statistically distinguishable from zero under its stated calculation, but the direction does not match the summary’s expectation that placebo may reduce experimental pain. The registry record does not explain this difference between the stated expectation and the posted outcome direction.

That result should not be taken as proof that placebo increases pain, or as evidence that placebo is ineffective in other settings. It is a condition comparison from one study involving experimental contact-heat pain, using the reported VAS measurement and a specific crossover PET-fMRI design. The registry does not provide enough detail about the paired analysis, condition order, or participant-level results to identify an explanation or establish how the result generalizes.

The stated aim also concerns differences between people with migraine and healthy participants. The aggregate outcome summaries do not present separate estimates for those populations or a test of whether their responses differ. In addition, the registry summary describes episodic migraines, while the stated hypothesis refers to chronic migraine patients. The record does not clarify that distinction, so the posted outcomes should not be treated as a direct test of a clearly specified migraine subgroup comparison.

The secondary imaging measures may contribute to understanding brain responses associated with the conditions, but the reported signals do not establish a mechanism. A lack of a clear PET contrast does not prove that opioid-related processes are absent, and BOLD contrasts alone do not identify the cause of a pain-rating difference. The registry does not report enough analysis detail to connect these measurements causally.

In sum, the results are informative as recorded condition-level summaries, but their interpretation is limited by the crossover analysis details, unadjusted secondary testing, and the absence of group-specific estimates and a fully reported analysis plan.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a subjective pain outcome with brain-imaging measures in a randomized crossover design. That design can make within-person comparisons valuable: each participant may contribute information under more than one condition. At the same time, the design requires analysis methods that account for the pairing and possible period or order effects. The registry identifies the design but does not report enough participant-level or model information to assess those features.

The results also illustrate why effect direction, statistical evidence, and scientific expectation need to be considered separately. The registry describes an interest in placebo analgesia, yet the posted mean VAS rating is lower in the no-intervention condition. Statistical significance does not explain that direction or reconcile it with the stated hypothesis. Reading the numerical contrast alongside the outcome description helps prevent a p-value from being treated as a complete scientific conclusion.

The use of several secondary imaging outcomes raises a further statistical issue: multiple comparisons can produce apparently notable results even when each individual test is unadjusted. The record does not report a multiplicity strategy. The different pattern across fMRI and PET outcomes underscores the importance of prespecification and cautious interpretation rather than selecting only the results that appear most consistent with an expected mechanism.

Finally, the study’s stated comparison between migraine and healthy participants is not visible in the aggregate posted outcome summaries. This highlights the distinction between a study’s motivating question and the specific contrasts that its registry results allow readers to evaluate. Clear reporting of subgroup estimates, crossover models, missing-data handling, and outcome hierarchy would strengthen interpretation of both the clinical and imaging results.

18. Limitations

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

Several trial-specific limitations affect interpretation. The registry identifies a crossover design but does not report condition order, washout, period effects, carryover assessment, or the paired analysis model. The posted recalculations use condition-level summary statistics, and the participant-level paired differences and within-person correlation are not reported. This limits assessment of the precision and appropriateness of the recalculated contrast for the design.

The registry’s description of the migraine population is not fully consistent: the brief summary describes episodic migraines, while the hypothesis refers to chronic migraine patients. The record does not clarify whether both descriptions refer to the population enrolled or to different aims. The posted outcome summaries are not broken out by migraine and healthy status, so they do not show the population-specific effects or a condition-by-population comparison.

The outcome direction also differs from the expectation stated in the primary outcome description. The record does not explain whether this reflects the experimental context, measurement, analysis, or another factor. No clinical-importance threshold is reported for interpreting the VAS contrast.

Additional limitations include the absence of a detailed statistical analysis plan, a reported multiplicity strategy, missing-data procedures, and outcome-specific analysis populations. The masking description does not identify who was masked. Some secondary outcome analysis details are not reported, and the imaging methods are not described in sufficient detail to assess processing or regional analysis choices. These are reporting limitations; the registry record alone cannot establish whether the procedures were absent or simply not posted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Molecular and Functional PET-fMRI Measures of Analgesia in Migraine — NCT01970943.
• Registry record last updated 2019-05-17; status last verified 2019-05.
• Results first posted 2019-05-17.
• 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.

22. Record Summary

NCT01970943 is a completed, randomized, single-masked crossover study sponsored by Massachusetts General Hospital. It investigated placebo-related experimental pain and PET-fMRI measures in people with migraine and healthy participants. The registry lists an enrollment of 23, a start date of 2012-09-01, and primary completion on 2014-04-30.

The primary outcome was mean VAS pain rating on a 0–10 scale. The posted mean was 4.3 in the no-intervention condition and 7.2 in the placebo condition; the recalculated contrast was -2.9, with a 95% confidence interval from -4.407 to -1.393 and an unadjusted p-value < 0.001. Three secondary outcomes cover fMRI BOLD signals and PET diprenorphine.

The posted results require cautious interpretation because the crossover analysis details, group-specific outcomes, missing-data procedures, and multiplicity plan are not reported. The aggregate summaries describe condition differences but do not directly answer whether responses differed between migraine and healthy participants.