Transcranial Alternating Current Stimulation in Back Pain- Pilot Sudy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Transcranial Alternating Current Stimulation in Back Pain- Pilot Sudy (NCT03243084), a randomized na study. The primary outcome is Change in Heart Rate Variability Before and After 40-minute Stimulation.

2. Clinical Question

3. Trial Design

The registry describes a completed randomized, double-masked crossover pilot study of active tACS and sham stimulation for chronic low back pain. Enrollment was 21. In a crossover design, participants receive more than one study condition, so comparisons may be made within participants. The registry record does not report the order or sequence of conditions, whether sequence assignment was balanced, or whether a washout period was used. Those details are important for judging potential period or carryover effects, but they cannot be inferred from the design label alone.

The active condition was 10 Hz stimulation at 2mA for 40 minutes. The sham condition used the same device family and was described as mimicking physical stimulation, with up to one minute of stimulation in a session. The record identifies the trial as double-masked but does not specify which roles were masked or how the success of masking was assessed.

The primary outcome was change in heart rate variability before and after a 40-minute stimulation session at each session. The registry lists the outcome as a mean with standard deviation and gives ms^2 as its unit. Change in pain rating on a visual analog scale before and after a 40-minute stimulation session was a secondary outcome. The record lists three outcome measures and two analyses, while one secondary outcome is posted in the posted outcome information. The timing of follow-up beyond the stimulation sessions is not reported in the registry record.

The trial is marked completed, with start and primary completion dates of 2017-09-07 and 2017-12-31. Its stated aims included assessing feasibility, collecting pilot efficacy information, and gathering EEG and EKG biomarker data to inform later study design. The original design assumptions, including any planned sample-size justification, 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.

Session 1

Washout (1-3 Weeks)

Reasons for not completing this period:

Session 2

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change in Heart Rate Variability Before and After 40-minute Stimulation, measured over before and after 40-minute stimulation at each session.

The primary endpoint was change in heart rate variability before and after 40-minute stimulation at each session. Heart rate variability describes variation in the timing between heartbeats; the registry specifically frames this outcome as a measure related to parasympathetic tone and high-frequency input assessed through spectral analysis of EKG recordings. Its unit is ms^2, and the posted summaries are means with standard deviations.

A before-and-after change outcome focuses on how the measure shifted during a stimulation session, rather than on the post-session value alone. The comparison of active and sham conditions is intended to help distinguish changes associated with active stimulation from changes that may occur during a sham session or over the same measurement period. Because the design is crossover, the conditions are intended to be compared within the trial’s crossover structure; the registry’s posted group summaries do not explain how that structure was handled in the reported analysis.

The endpoint is a physiological measure, not a direct measure of pain relief or everyday function. The registry describes it as a biomarker-related outcome and states that the study aimed to collect pilot efficacy and EEG and EKG data. The choice can therefore be understood as addressing a proposed physiological mechanism alongside a separate secondary pain-rating measure. The registry does not report a threshold for a clinically important change in heart rate variability, nor does it provide enough detail to determine how the endpoint was selected or how its clinical relevance was defined.

7. Results Posted in the Registry

• Active10 Hz tACS: mean -0.01 versus 0.21 on control; difference -0.22 (95% CI -0.63 to 0.20), standardized effect d = -0.32; z-test p = 0.306.

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 Pain Rating on the Visual Analog Scale Before and After 40-minute Stimulation

• 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:
  • Active 10 Hz tACS: mean 0.18 versus -0.18 on control; difference 0.36 (95% CI -0.09 to 0.80), standardized effect d = 0.50; z-test p = 0.116.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active 10 Hz tACS and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns change in visual analog scale pain rating before and after a 40-minute stimulation session. The recalculated mean difference is 0.358, and its interval includes zero. The sponsor’s rank-based analysis reports a p-value just below the 0.05 planning threshold, whereas the simple unadjusted mean comparison has a p-value of 0.116. This contrast reflects the use of different methods; it should not be treated as a simple confirmation by one analysis of the other.

Across the primary and secondary outcomes, the primary comparison does not show a clear difference in the posted summaries, while the secondary result is more sensitive to which analysis is considered. That pattern is not enough to establish a consistent treatment effect across physiological and pain measures. The outcomes address different constructs, and the registry does not report a planned relationship between changes in heart rate variability and changes in pain rating. Nor does it establish how a particular direction of change on the pain scale should be interpreted as improvement.

Unadjusted secondary results carry less weight because multiple outcomes or analyses create more opportunities for a nominally notable result. The registry lists three outcome measures and two analyses, but it does not report whether multiplicity was addressed, whether all analyses were prespecified, or how the outcomes were prioritized beyond identifying the primary outcome. The registry-reported secondary p-value should therefore be treated as exploratory, particularly in a pilot study. It may inform future research questions, but it should not override the primary outcome or be interpreted as definitive evidence on its own.

The record posts one secondary outcome in the outcome information described for these results. Information on the remaining outcome measures and any additional analyses is not reported in the registry record. That limits assessment of the full set of outcomes considered and the potential for selective emphasis.

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

• Change in Pain Rating on the Visual Analog Scale Before and After 40-minute Stimulation

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary summaries describe a continuous outcome using means and standard deviations. A mean gives the arithmetic average of observed change scores in a condition; the standard deviation describes how spread out those scores are around the mean. The active-minus-sham mean difference compares the two condition averages. A negative contrast means the active-condition mean was lower than the sham-condition mean under that subtraction order. It does not, by itself, establish whether that direction represents improvement, because the registry does not state a directional interpretation for the change score.

What does the confidence interval represent?

A confidence interval expresses uncertainty around an estimated effect under the statistical method used to construct it. A narrower interval indicates greater precision, while a wider interval indicates less precision. For the recalculated primary comparison, the interval spans both sides of zero. Zero represents no mean difference under the contrast being estimated, so an interval that includes zero is compatible with no difference as well as with differences in either direction. The interval should not be read as a range containing a fixed percentage of individual participants’ outcomes.

How should the p-values be read?

A p-value describes how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor is it a measure of the size or importance of an effect. The recalculated primary p-value is unadjusted and comes from a simple comparison of posted summaries. The registry’s primary analysis is identified as ANOVA and reports p = .319. The record does not give the ANOVA model specification, so the two p-values should not be expected to match exactly or be interpreted as the same calculation.

The secondary analysis illustrates why method matters. Its registry-reported method is Wilcoxon (Mann-Whitney), a rank-based comparison that evaluates the ordering of observations rather than directly testing a difference between means under the same assumptions as a standard mean comparison. The simple recalculation instead uses posted means and standard deviations to estimate a mean difference. These methods can yield different p-values because they address the data through different summaries and assumptions. The registry’s record does not provide the individual observations or further analysis details needed to reconcile the secondary results.

Why does the crossover design matter?

A crossover design allows participants to receive both conditions, potentially making each participant’s responses informative for the comparison. This can account for stable differences between participants if the analysis appropriately models paired or repeated observations. However, the registry’s posted arm summaries alone do not show whether the recalculation accounts for within-participant pairing. Nor does the record describe the condition sequence, period effects, carryover assessment, or the sponsor’s treatment of repeated measurements. The simple recalculation should therefore be understood as an unadjusted comparison of posted summaries, not as a definitive analysis of the crossover data.

General statistical principle: repeated measurements from the same participant are usually correlated rather than independent. An analysis that ignores this correlation may misstate uncertainty, while an analysis that accounts for it requires information about the within-person structure. The registry identifies ANOVA for the primary sponsor analysis but does not report enough detail to determine how repeated measurements or crossover periods were represented in that model.

What is over-dispersion?

General statistical principle: over-dispersion occurs when observed variability exceeds what a statistical model assumes. It is especially relevant to count outcomes and some generalized models. The posted primary and secondary outcomes are continuous measures summarized with means and standard deviations, and the registry does not report a model or finding described as over-dispersion. It is therefore not a specific reported issue for these results. More generally, the variability in the posted summaries matters because uncertainty in an estimated difference depends on both effect size and outcome spread.

The standard deviations differ between conditions in the posted summaries, particularly for the pain-rating outcome. A simple pooled standard deviation is used in the recalculated standardized effect, but that standardized value is not the sponsor’s reported primary result. Standardization can help describe an effect relative to observed variability; it does not resolve the crossover-analysis questions or supply a clinical threshold.

Finally, multiplicity concerns arise when several outcomes or analyses are examined. With multiple opportunities to find a result that appears statistically notable, an unadjusted p-value can overstate the strength of evidence if interpreted as though it were the only test. The registry lists three outcome measures and two analyses, but does not report a multiplicity adjustment or a prespecified hierarchy beyond identifying the primary outcome. The secondary result should therefore be interpreted more cautiously than a single, prespecified primary comparison.

11. Confidence Intervals and Precision

The primary recalculated mean difference is -0.216, with a confidence interval that runs from below zero to above zero. This interval communicates substantial uncertainty about both the direction and the size of the contrast. It includes zero, so the posted summaries do not rule out no mean difference. It also permits effects in either direction, rather than tightly locating the effect around one value.

Precision is distinct from statistical significance and clinical importance. The interval gives a range of effect sizes compatible with the data and the calculation’s assumptions; it does not say that every value in that range is equally likely. It also does not establish whether any particular effect would matter to patients or clinicians. The registry does not report a clinically important threshold for heart rate variability change, so the clinical meaning of the interval’s endpoints cannot be classified from the record alone.

The calculation is based on posted summary statistics and is explicitly unadjusted. The study is described as crossover, but the recalculation does not incorporate a reported within-participant correlation or an identified crossover model. That limits how directly its precision estimate can be applied to the design. The sponsor’s ANOVA p-value is reported, but a sponsor-reported effect estimate and confidence interval are not available in the registry record.

The secondary pain-rating interval also spans zero in the simple recalculation, while the sponsor-reported rank-based analysis has a p-value just below the stated 0.05 planning threshold. The differing methods reinforce that statistical conclusions can depend on the analysis chosen. Both outcome results should be interpreted in the context of the pilot’s limited enrollment, the absence of an original design justification in the registry record, and the lack of detail about missing observations and analysis populations.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario targets an effect equal to the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective planning quantities, not a description of what happened in this completed pilot.

The rows consider planning for 100%, 75%, and 50% of the observed effect. As the effect being planned for becomes smaller, more participants are needed to distinguish it from random variation at the same significance level and target power. The figures are sensitive to the observed effect used as their starting point, so a pilot estimate can make planning numbers unstable. Smaller or larger effects in a future study would change the required sample size.

These figures are not observed power. Observed power is not a useful substitute for interpreting the estimated effect and its uncertainty after a study has been completed. The original trial’s sample-size assumptions and justification are not reported in the registry record; the planning figures should not be mistaken for those original assumptions. They also use an equal-allocation, two-arm framing and do not show how a future crossover design, repeated measurements, missing data, or a different analysis would affect planning.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.216; pooled standard deviation σ = 0.668.
2. n = 2 × (1.96 + 0.842)² × 0.668² / -0.216² = 149.9, rounded up to 150 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.216                      # observed difference in means
sigma <- 0.667532770731145                     # 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(3243084)
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 = 150 (80% power), 201 (90% power)
 75% of observed effect: n per arm = 267 (80% power), 357 (90% power)
 50% of observed effect: n per arm = 600 (80% power), 803 (90% power)
power.t.test: 150.9 
Simulated power at n = 150 per arm: 0.793 (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

For the primary outcome, the registry reports an ANOVA with p = .319. The simple unadjusted recalculation from the posted means and standard deviations gives a mean difference of -0.216, a confidence interval that crosses zero, and an unadjusted p-value of 0.306. The recalculation and sponsor-reported analysis are related to the same primary comparison, but they are not the same analysis: the recalculation uses posted summary statistics and does not incorporate a documented crossover model.

The registry does not report the sponsor ANOVA’s effect estimate, confidence interval, model specification, or handling of within-participant data. As a result, the recalculated estimate is useful as a transparent descriptive comparison, but it cannot be presented as a reproduction of the sponsor’s analysis. The record does not flag a discrepancy between the sponsor result and the recalculation.

For the secondary pain outcome, the sponsor reports a Wilcoxon (Mann-Whitney) analysis, while the simple recalculation compares means. The registry-reported p-value is just below the stated 0.05 planning threshold, while the unadjusted recalculated p-value is 0.116. These results differ in method and estimand, so the comparison is not a like-for-like check of a single test. The sponsor’s own result should be read as the registry-reported analysis, with the limitations of the unreported model details and multiplicity plan kept in view.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies heart rate variability change as the primary outcome and pain-rating change as a secondary outcome. It also lists three outcome measures and two analyses. Testing multiple outcomes or using multiple analysis choices can increase the chance that at least one result appears notable by chance. A multiplicity strategy can address that issue, for example by defining a hierarchy or adjusting the interpretation of tests. Such a strategy is not reported in the registry record.

It is also not reported whether the outcomes, analysis methods, and time points were prespecified in a protocol or statistical analysis plan, or whether any analyses were conducted after examining the data. The registry record does not describe interim analyses. These omissions do not establish that such practices occurred; they mean that readers cannot assess them from the posted record.

The crossover label raises questions about the analysis population and treatment of repeated observations. The registry does not report whether the analyses used all randomized participants, all participants with data in both conditions, or another population. It does not describe missing-data amounts, reasons for missingness, imputation, exclusions, or sensitivity analyses. Nor does it specify how sequence, period, or possible carryover effects were handled. These details matter because the analysis of a crossover study depends on observations linked within participants and on the order and timing of conditions.

The registry lists different at-risk counts for the serious-adverse-event summaries and outcome summaries. It does not explain the reasons for those differences or provide a participant-flow account that connects enrollment, treatment exposure, outcome measurement, and analysis. The record also does not report whether any analysis adjusted for baseline values or other covariates. Without these details, the posted results can be described, but the robustness of the analysis to missingness, exclusions, and modeling choices cannot be established.

The original sample-size justification and statistical analysis plan are not reported in the registry record. The planning illustrations based on the observed effect are not a substitute for either. This limits the ability to judge whether the trial was designed around a specific clinically meaningful effect or how the statistical analysis was intended to address the crossover structure and multiple outcomes.

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.

The registry reports zero serious adverse events in the sham group and zero in the active 10 Hz tACS group. It also reports zero other adverse events and zero deaths in each group. The serious-adverse-event at-risk counts are 21 for sham and 20 for active stimulation; the other-adverse-event at-risk counts are also 21 and 20, respectively. These counts describe the posted safety record, not proof that no adverse events could occur.

The registry does not list serious adverse-event terms, consistent with the posted zero serious events. It does not provide further detail on how events were defined, collected, graded, or attributed to a condition. The at-risk counts differ from the outcome-summary counts, and the record does not explain the distinction. Safety findings from this pilot should be interpreted within the limited scope of the reported observations and follow-up; duration of follow-up for adverse events is not reported in the registry record.

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

The posted primary summaries show a small difference in average heart rate variability change between active and sham conditions, with an unadjusted recalculated mean difference of -0.216. The confidence interval crosses zero, and the sponsor-reported ANOVA has p = .319. These results do not provide a precise estimate of the primary comparison. They do not establish that the conditions are equivalent, and they do not rule out effects in either direction.

The secondary pain-rating analysis has a different pattern depending on the method: the sponsor’s rank-based test has a p-value just below the stated 0.05 planning threshold, while the unadjusted mean comparison has a p-value of 0.116 and an interval that includes zero. This method dependence, combined with the lack of a reported multiplicity plan, means the secondary result should be considered exploratory. It does not establish clinical benefit or a reliable pain effect.

The trial’s aims included feasibility and collection of pilot efficacy and biomarker data, so its results can be understood as preliminary. The registry’s stated physiological rationale concerns presumed alpha-oscillation structure in the prefrontal cortex, but the posted primary endpoint is heart rate variability. The record does not establish that a change in this biomarker corresponds to a meaningful change in pain or function.

The findings do not determine how the intervention should be used, and they are not medical advice. The registry does not report clinically important thresholds for either outcome, detailed crossover methods, a complete analysis plan, or enough information to assess missing data and the full set of analyses. Larger or differently designed studies could produce estimates with different precision. The posted observations alone cannot establish the effect in populations beyond the people enrolled in this pilot.

18. Why This Trial Matters Statistically

This trial is statistically informative as an example of the distinction between a pilot estimate and a definitive comparison. It reports continuous outcomes as means and standard deviations, while the primary sponsor analysis is identified as ANOVA and the secondary analysis as Wilcoxon (Mann-Whitney). Comparing those reported methods with simple recalculations makes clear that the choice of analysis affects what is estimated and how uncertainty is assessed.

The crossover design also highlights why summary statistics may not contain enough information to reconstruct an analysis. Within-participant comparisons can use the relationship between each participant’s responses under the conditions. That relationship is not captured in separate condition summaries. Without sequence, period, carryover, and model details, a simple recalculation is best understood as descriptive rather than as a substitute for the trial’s analysis.

The primary interval includes zero and extends in both directions, illustrating why a p-value alone is an incomplete account of evidence. The estimate and interval communicate the direction and precision of the observed contrast more directly. The registry does not report a clinically important threshold, so statistical evidence cannot be translated into a judgment about clinical importance.

Finally, the secondary result illustrates the role of multiplicity and analytic choices. A p-value just below a conventional threshold in one method should not be isolated from the number of outcomes, the primary result, and the other analysis. The absence of a reported multiplicity plan and analysis details limits certainty about how to weigh that result. These are practical considerations for biostatisticians and clinical researchers interpreting pilot and crossover studies.

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.

The enrollment was 21, and the posted outcome summaries list 20 observations in each condition. The registry does not explain the relationship between these counts, the crossover structure, or whether the same participants contributed to both condition summaries. The adverse-event at-risk counts also differ by condition, and the reason is not reported. Without a participant-flow description, it is difficult to assess exclusions, missing outcomes, or the analysis population.

Although the trial is labeled randomized, double-masked, and crossover, important implementation details are not reported in the registry record. These include sequence generation and allocation concealment, which roles were masked, how masking was assessed, the order of stimulation conditions, and whether a washout period was used. The record also does not describe how the primary ANOVA accounted for paired observations, session order, or period effects.

The simple recalculations use posted summary statistics and are unadjusted. They do not reconstruct a crossover model or incorporate a reported within-participant correlation. The sponsor’s primary analysis is named but not fully specified, and its effect estimate and confidence interval are not posted. The secondary mean comparison and sponsor-reported rank-based test do not estimate the same quantity in the same way.

The record does not report a multiplicity plan, original sample-size justification, clinically important thresholds, missing-data methods, or sensitivity analyses. It lists three outcome measures and two analyses, while the described secondary results include one outcome. The status of the other measures and any unreported analyses cannot be determined from the registry record. These limitations constrain confidence in the precision and generalizability of the posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Transcranial Alternating Current Stimulation in Back Pain- Pilot Sudy — NCT03243084.
• Registry record last updated 2018-12-12; status last verified 2018-01.
• Results first posted 2018-12-12.
• 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

The registry record describes a completed randomized, double-masked crossover pilot study of active 10 Hz tACS versus sham stimulation for chronic low back pain. Enrollment was 21, and the study dates are 2017-09-07 through primary completion on 2017-12-31. The stated aims included feasibility, pilot efficacy, and collection of EEG and EKG biomarker data.

The primary outcome was change in heart rate variability before and after 40-minute stimulation at each session. The sponsor reports an ANOVA with p = .319. A simple unadjusted recalculation from posted summaries gives a mean difference of -0.216, with an interval spanning zero. The secondary pain-rating result differs by analysis method and remains exploratory. The registry reports zero serious adverse events, zero other adverse events, and zero deaths in both groups. Key details on the crossover analysis, missing data, multiplicity, and the original sample-size rationale are not reported in the registry record.