Promoting Physical Activity in Churchgoing Latinas: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Promoting Physical Activity in Churchgoing Latinas (NCT01776632), a randomized na study. The primary outcome is Accelerometer-based Moderate-to-vigorous Physical Activity (MVPA).

2. Clinical Question

The question concerns a comparison between two assigned program conditions, not a comparison with no intervention. The control condition offered health education on cancer screening and prevention, so the contrast is between physical activity programming and an attention-control educational program. The registry states that churches were randomly assigned to a condition. That assignment structure matters when interpreting participant-level results because participants within the same church may share aspects of their environment and program experience.

The outcome was defined as change from baseline in moderate-to-vigorous physical activity, measured by accelerometer. The posted month-12 group values and the sponsor’s adjusted comparison are the available result summaries. The registry record does not report a month-24 result in the primary outcome information. It also does not report enough detail to determine all elements of the adjusted contrast or its uncertainty.

3. Trial Design

This was a randomized, parallel-group behavioral trial, recorded as double masked. The registry identifies San Diego State University as sponsor and lists the trial status as completed. The study began on 2011-05-11, with primary completion on 2015-12-21. Phase is listed as NA. The enrollment figure in the record is 436.

Random assignment occurred at the church level: the brief summary states that 16 churches were assigned to the physical activity intervention or the attention-control condition. This is a cluster-randomized structure, in which churches rather than individual participants are the stated units of assignment. The record does not identify who was masked, describe how masking was maintained, or give details of the randomization procedure. Those design details are not reported in the registry record.

The intervention condition was a multilevel Faith in Action program intended to promote physical activity. The comparator was a Faith in Action program concerning cancer screening and prevention. The summary describes the physical activity program as addressing environmental influences at the church, neighborhood, and community levels, as well as personal factors related to activity. Details of the delivered activities, their intensity, adherence, or implementation fidelity are not reported in the registry record.

The primary outcome was accelerometer-based moderate-to-vigorous physical activity, measured in minutes per week. The record says it was assessed at baseline, 12 months, and 24 months following implementation of intervention activities, while month 12 is the time point reported. Valid accelerometer data at month 12 were available for 183 participants in the physical activity condition and 186 in the cancer screening condition. The record says participants without valid data, including those with unmet wear-time requirements or a lost device, were excluded from that analysis.

Body mass index and waist circumference were listed as secondary outcomes, with month-12 results reported. The registry does not describe the original sample-size justification, any interim analyses, detailed masking procedures, or a full statistical analysis plan. Those features should not be inferred from the posted results.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: A total of 369 participants (183 physical activity condition, 186 cancer screening condition) had valid accelerometer data at 12-month follow-up measures. Those without valid data (unmet wear time, lost device, etc) were not included in the analysis.

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 Accelerometer-based Moderate-to-vigorous Physical Activity (MVPA), measured over assessed at Baseline, 12 and 24 months following implementation of intervention activities, month 12 reported.

The primary endpoint is accelerometer-based moderate-to-vigorous physical activity (MVPA), expressed in minutes per week. The registry describes the endpoint as change from baseline and states that measurement was scheduled at baseline, 12 months, and 24 months after intervention activities began. Month 12 is the time point reported in the registry results.

An accelerometer records movement over time, providing an objective activity measure rather than relying only on a participant’s recollection. In general, objective measurement can reduce some forms of recall error, though it still depends on usable device data and the wear-time rules used to define a valid record. The registry says that participants without valid accelerometer data because of unmet wear time, a lost device, or similar reasons were excluded from the month-12 analysis. It does not report further details about the device, processing rules, or how missing readings were handled.

MVPA is relevant to the trial’s stated aim because the intervention was designed to promote physical activity. Measuring activity in minutes per week gives a continuous outcome, so the group summaries can describe both average activity and its variability. The primary question is comparative: whether the physical activity condition produced a different month-12 result from the cancer screening and prevention condition. The endpoint itself does not establish why a difference might occur, and a group average does not describe every participant’s experience.

7. Results Posted in the Registry

• Cancer Screening: mean 129.90 versus 144.40 on control; difference -14.50 (95% CI -39.35 to 10.35), standardized effect d = -0.12; z-test p = 0.253.

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.

Body Mass Index (BMI)

• 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:
  • Cancer Screening: mean 30.60 versus 30.18 on control; difference 0.42 (95% CI 0.03 to 0.81), standardized effect d = 0.22; z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Cancer Screening than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Waist Circumference

• 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:
  • Cancer Screening: mean 96.56 versus 95.20 on control; difference 1.36 (95% CI -0.07 to 2.79), standardized effect d = 0.20; z-test p = 0.062.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cancer Screening and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes are body mass index and waist circumference, both reported at month 12. Taken together, their results add context about measures related to body size, but they do not replace the primary activity endpoint. The posted pattern is mixed rather than a uniform confirmation across the secondary outcomes: the sponsor’s adjusted analyses differ in the strength of their statistical evidence, and the unadjusted recalculations do not provide a consistent basis for treating every secondary result as conclusive.

Secondary endpoints are usually interpreted more cautiously than a prespecified primary endpoint. They may be exploratory, and the more outcomes examined, the greater the chance that at least one result will appear noteworthy by chance if no adjustment is made. The registry record does not report whether multiplicity was controlled, whether these secondary outcomes were prespecified in a detailed analysis plan, or how the sponsor prioritized them. Without that information, isolated secondary findings should carry less weight than a result supported by a clearly specified primary analysis.

The secondary outcomes also have their own measurement and analysis considerations. The posted values are means with standard errors, and the sponsor reports mixed-effects models. The registry does not give the model details, confidence intervals for the adjusted estimates, or a complete account of missing data for these outcomes. As with the primary endpoint, the adjusted and unadjusted analyses are not identical estimands. The available secondary results therefore support a cautious, descriptive reading rather than a broad claim about the intervention’s effects on body size.

The overall relationship to the primary result is limited: secondary findings can provide supporting or contrasting context, but they do not resolve the discrepancy between the primary sponsor analysis and the unadjusted recalculation. Nor can they establish a mechanism linking physical activity programming to changes in these measures. The registry record does not report an analysis that formally tests whether secondary changes mediate or explain the primary outcome.

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

• Body Mass Index (BMI)
• Waist Circumference

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean amount of activity in minutes per week. For a continuous measure, the group mean describes the center of the observed values, while the standard deviation describes how spread out participant values are around that mean. These quantities answer different questions. A mean difference describes a contrast in average activity; a standard deviation describes variation among individuals within a group.

What does the unadjusted comparison represent?

The recalculated comparison uses the posted group means and standard deviations to form a simple, unadjusted contrast. It does not incorporate baseline values, covariate adjustment, or any other structure beyond the summary-statistic calculation. For the primary result, the recalculated mean difference is -14.5 minutes/week when expressed as cancer screening relative to physical activity. The recalculated pooled standard deviation is 121.8, and the standardized effect estimate is -0.119. These standardized quantities put the observed difference on a scale relative to variability, but they do not replace the original minutes-per-week measure.

The posted group standard errors are 8.715 and 9.209. A standard error describes uncertainty in an estimated mean, rather than individual variability. In general, standard errors tend to be smaller than standard deviations because they concern the precision of a group estimate rather than the spread of participant measurements. The registry lists standard deviations for the primary outcome, and the comparison information also includes standard errors.

What does a confidence interval add?

A confidence interval gives a range of values compatible with an estimate under the method used to construct it. It conveys precision in a way that a point estimate alone cannot. The unadjusted primary interval extends from -39.35 to 10.35 minutes/week. Because that range includes zero, the recalculated summary-statistic comparison is compatible with no mean difference as well as with values on either side of zero. The interval is for the unadjusted recalculation; it is not an interval for the sponsor’s adjusted estimate.

A p-value addresses a different question. In general, it describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and analysis model. It does not measure the size of an effect, the probability that a treatment is beneficial, or the importance of an outcome. The recalculated primary p-value is 0.253; the sponsor’s reported adjusted p-value is .03. The difference reflects that the analyses are not the same and should not be interpreted as if they were duplicate calculations of an identical model.

Why use a mixed-effects analysis?

The sponsor reports a generalized linear mixed effects analysis for the primary endpoint. In general, mixed-effects models can represent related observations by including model components for grouping or repeated measurement. In a church-randomized study, people enrolled through the same church may have correlated outcomes. A model that represents such grouping can be more appropriate than treating every participant as wholly independent, depending on its specification. The registry record does not state the model’s random effects, fixed effects, covariance structure, or other details, so it is not possible to verify precisely how the model handled church-level clustering or repeated assessments.

The sponsor reports a difference of adjusted means, whereas the recalculation is an unadjusted comparison of posted summary statistics. Adjustment may account for prespecified variables or design features, but the exact variables and procedures are not reported in the registry record. The adjusted estimate therefore cannot be reconstructed from the posted group means and standard deviations alone. Since the registry record marks a discrepancy between the sponsor’s analysis and the simple recalculation, the sponsor’s own analysis takes precedence for interpreting the trial’s reported inferential result.

Why can clustering matter?

General statistical explanation: when participants share a church, their outcomes may be more alike than outcomes from participants in different churches. This dependence is often called intracluster correlation. If an analysis treats correlated observations as independent, its uncertainty can be misstated. Accounting for clustering may change standard errors and confidence intervals, even when the group means themselves are similar. The number of churches and the assignment of churches are therefore relevant to interpreting the design. The registry reports 16 randomly assigned churches, but does not provide the estimated within-church correlation or enough model detail to assess its handling.

Variation can also be greater than a simple model assumes. General statistical explanation: over-dispersion means that observed variability exceeds what a model’s basic assumptions would predict. Allowing for extra variability can affect uncertainty estimates and tests. The registry does not report a diagnosis of over-dispersion for this outcome, so it would be inappropriate to claim that it occurred or that a particular correction was used.

Finally, the primary result applies to the analysis population with valid month-12 accelerometer data. Excluding participants without valid measurements may affect representativeness if availability of valid data is related to activity or other characteristics. The record describes some reasons for exclusion but does not report a missing-data model, imputation, or sensitivity analysis. These omissions limit assessment of how robust the reported comparison is to incomplete measurement.

11. Confidence Intervals and Precision

The unadjusted primary comparison has a mean difference of -14.5 minutes/week, with a confidence interval from -39.35 to 10.35. The interval spans zero, so the posted summary-statistic recalculation does not sharply distinguish a negative contrast from a positive one. Its width indicates that the estimate is not highly precise on the minutes-per-week scale. This is a statement about uncertainty in the unadjusted comparison, not about the sponsor’s adjusted model.

The sponsor’s adjusted estimate is 0.15, with p = .03, but the registry record does not report a confidence interval or confidence level for that result. A p-value alone cannot show the range of effect sizes compatible with the adjusted analysis. It is therefore not possible to describe the precision of the sponsor’s adjusted estimate from the registry result as posted. The sponsor’s analysis remains the primary reported inferential result because the record identifies a discrepancy with the simple recalculation.

In general, precision depends on more than the number of analyzed participants. Variability in the outcome, clustering by church, missing measurements, the model specification, and the distribution of participants across churches can all matter. The posted standard deviations—117.9 for the physical activity condition and 125.6 for the cancer screening condition—show notable dispersion in individual activity values. The record does not report the within-church correlation or model details needed to translate the design into a complete assessment of precision.

The distinction between statistical precision and practical importance is also important. A confidence interval concerns uncertainty in an estimated contrast; it does not by itself establish whether an effect matters to participants or how it relates to health outcomes. The registry does not state a threshold for a meaningful difference in MVPA. Without that threshold and without an interval for the adjusted result, the clinical or practical importance of the adjusted estimate cannot be evaluated from the posted primary analysis alone.

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 illustrations are expressed as participants per arm, not as total events. They use the observed effect as a reference and show planning values for detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. These are assumptions for the planning illustration; the trial’s original sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, the illustration gives participants per arm for 80% power and participants per arm for 90% power at each stated fraction of the observed effect. For example, planning for 100% of the observed effect gives 1,109 participants per arm for 80% power and 1,484 participants per arm for 90% power. Planning for 75% gives 1,971 and 2,638 participants per arm, respectively; planning for 50% gives 4,434 and 5,936. The pattern is the key point: smaller effects require more participants to detect under the same assumptions.

In general, 80% power means that a study designed under the stated assumptions would have an 80% chance of rejecting the null hypothesis if the effect used for planning were the true effect. The 90% column represents a higher target chance under those same assumptions and therefore calls for a larger planned sample. These figures are not observed power. They are planning illustrations based on the observed effect, not a reconstruction of the trial’s actual design calculations.

The curve should be read as another representation of the relationship between the assumed effect size and the participants required. It does not describe the number of participants actually analyzed, and it does not account for unreported design features unless explicitly included in its stated assumptions. In particular, the illustration specifies equal allocation and a normal approximation; the registry record does not report whether the original design incorporated a cluster-randomization adjustment or other allowances.

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 = -14.500; pooled standard deviation σ = 121.842.
2. n = 2 × (1.96 + 0.842)² × 121.842² / -14.500² = 1,108.4, rounded up to 1,109 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 <- -14.5                      # observed difference in means
sigma <- 121.842309085878                     # 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(1776632)
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 = 1,109 (80% power), 1,484 (90% power)
 75% of observed effect: n per arm = 1,971 (80% power), 2,638 (90% power)
 50% of observed effect: n per arm = 4,434 (80% power), 5,936 (90% power)
power.t.test: 1109.4 
Simulated power at n = 1,109 per arm: 0.791 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as a generalized linear mixed effects model of adjusted means, with an estimate of 0.15 and p = .03. The registry does not report a confidence interval for this estimate. The simple recalculation instead compares the posted group summaries without adjustment and gives a mean difference of -14.5 minutes/week for cancer screening relative to physical activity, with a confidence interval from -39.35 to 10.35 and p = 0.253.

These values should not be treated as interchangeable. The sponsor’s adjusted model and the unadjusted recalculation differ in analytic approach, and the posted information is insufficient to reproduce the adjusted model. The record explicitly identifies a discrepancy. In that situation, the sponsor’s own analysis takes precedence; the recalculation is best understood as a transparent comparison derived from the posted summary statistics, not as a replacement for the trial’s model-based result.

The registry classifies the sponsor’s result as a superiority analysis. Its direction should be interpreted cautiously because the result does not fully specify the contrast orientation, and its precision cannot be judged without a confidence interval. The record does not describe the adjustment variables, model specification, or complete statistical plan, so the reason for the divergence from the simple recalculation cannot be established from the registry information alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or comparisons are tested. In general, conducting more tests increases the chance that at least one result will appear statistically unusual even when there is no corresponding underlying effect. A multiplicity plan may define which outcome is primary, specify an order for testing, or adjust the interpretation of secondary tests. The registry identifies one primary outcome and lists BMI and waist circumference as secondary outcomes, but does not report whether any multiplicity adjustment was used. The original statistical analysis plan and details of prespecification are not reported in the registry record.

Missing outcome data are relevant to the primary analysis. The record states that 369 participants had valid accelerometer data at month 12: 183 in the physical activity condition and 186 in the cancer screening condition. Participants without valid accelerometer data, including those with unmet wear time or a lost device, were excluded from the analysis. The record does not report the reasons for missing data beyond these examples, the characteristics of participants with and without valid data, or whether the missingness differed by condition.

Exclusion of records without valid measurement is a description of the analysis population, not a complete missing-data strategy. The registry does not report imputation, weighting, sensitivity analyses, or assumptions about whether missing activity measurements were related to participants’ unobserved activity levels. Consequently, the possibility of bias from incomplete measurement cannot be assessed using the registry information alone. The month-12 findings describe participants with usable accelerometer data, and the record does not establish how well that group represents all enrolled participants.

The secondary outcomes also have analysis populations that are not identical to the primary outcome population: the posted BMI and waist circumference summaries include their own group-specific participant counts. No explanation of the differences among these analysis populations, or of the handling of missing secondary measurements, is reported. Baseline measurements are mentioned as part of the assessment schedule, but the registry does not describe how baseline values entered the sponsor’s adjusted models.

Important statistical details remain unavailable, including the full covariate set, the treatment of church-level clustering, the handling of repeated measurements, and whether interim analyses occurred. These omissions do not invalidate the reported results by themselves, but they limit independent evaluation of the analysis choices and of the uncertainty around the adjusted estimates.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports no serious adverse events among participants at risk in either condition: 0 of 217 in the physical activity condition and 0 of 219 in the cancer screening condition. It separately reports other adverse events of 1 among 217 at risk in the physical activity condition and 0 among 219 at risk in the cancer screening condition. Deaths are listed separately as 1 in the physical activity condition and 0 in the cancer screening condition.

These counts are descriptive and should be read according to the categories used in the registry. The record does not list serious adverse event terms, and it does not state whether the other adverse event or the death was considered related to an intervention. The denominators shown are the groups at risk for the corresponding safety reporting. The counts do not establish that an event was caused by a program or that no unrecorded events occurred; they summarize the safety information entered in the registry record.

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

The posted results describe a randomized comparison of a multilevel physical activity program with a cancer screening and prevention education condition among Latina churchgoers. The primary measure was accelerometer-based MVPA at month 12. The registry presents both group summaries and a sponsor-reported adjusted analysis, but the two approaches yield different inferential results. The raw summary-statistic recalculation has a confidence interval that includes zero, while the sponsor reports an adjusted estimate with p = .03 and no confidence interval.

That difference means readers should distinguish the analyses rather than selecting whichever result appears more persuasive. The sponsor’s model-based analysis takes precedence over the recalculation, but the limited model details and the absent adjusted confidence interval make its size and precision difficult to assess independently. The unadjusted recalculation remains useful as a check on the posted means, but it is not a substitute for the sponsor’s analysis.

The result does not establish that the intervention caused a change for every participant, nor does an average group result describe individual responses. The analysis includes only participants with valid month-12 accelerometer records, and the registry does not report enough about missingness to determine whether exclusion altered the comparison. It also reports no month-24 primary result, even though that assessment time is listed.

General interpretation: statistical evidence and practical importance are different. A p-value does not show whether a difference is meaningful to participants, while a point estimate without a confidence interval cannot communicate the range of plausible adjusted effects. The registry does not report a threshold for a meaningful change in MVPA. The findings therefore should be understood as results from the reported analyses, with uncertainty and reporting limitations, rather than as a definitive statement about broader health effects or outcomes outside the trial’s measured endpoints.

The study’s setting also defines the scope of interpretation. The trial concerned Latina churchgoers recruited through churches and compared two behavioral programs. The registry record does not establish how findings would apply in other populations, settings, or program formats. It also does not report cancer outcomes or other clinical endpoints as primary results. The posted evidence addresses the specified activity measure and listed secondary body-size measures.

18. Why This Trial Matters Statistically

This trial is statistically instructive because the assignment occurred by church while the main outcome was measured for individual participants. Cluster assignment can create dependence among participants from the same church, making the analysis model and uncertainty calculation especially relevant. The record identifies a mixed-effects analysis, but does not provide the details needed to inspect how that structure was represented. This makes the distinction between the design and the participant-level summary important.

The record also illustrates why an adjusted sponsor analysis and a recalculation from summary statistics may not agree. The group means alone cannot recover a model that adjusts for unreported variables or represents design features. Here, the raw comparison and sponsor result differ, and the sponsor’s analysis takes precedence. Reporting the model specification and an interval for the adjusted estimate would make the result easier to evaluate.

Missing measurement is another central statistical issue. Valid accelerometer data were required for the primary analysis, and participants without such data were excluded. The number of analyzable records is therefore not the same as the enrollment figure. Without a fuller account of missingness, readers cannot determine whether the analyzed participants represent everyone enrolled or whether missingness may have affected the estimated comparison.

Finally, the secondary outcomes and planning illustrations show why statistical interpretation requires context. Several outcomes do not automatically constitute independent confirmation, especially when the record does not describe multiplicity control. Planning values derived from the observed effect are useful for illustrating how assumptions affect required sample sizes, but they do not explain the original design or quantify what the completed trial achieved. Together, these features make transparent reporting of design, models, missing data, and uncertainty essential for interpreting clinical trial evidence.

19. Limitations

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

Several limitations specific to the registry record constrain interpretation. Although 16 churches were randomly assigned, the record does not report the number of churches allocated to each condition, the randomization procedure, or the balance of participant enrollment across churches. It also does not report how clustering was handled in detail, despite the church-level assignment. The sponsor’s mixed-effects method is named, but its model terms and assumptions are not described.

For the primary endpoint, only participants with valid accelerometer data were analyzed at month 12. The record gives examples of why records could be invalid but does not report a comparison of included and excluded participants, a missing-data strategy, or sensitivity analyses. It therefore is not possible to assess whether the available accelerometer records could have produced a different comparison from a complete-data analysis. The registry reports the month-12 result but not the month-24 result, despite listing month 24 in the assessment schedule.

The sponsor’s adjusted primary estimate has no reported confidence interval, and the registry does not describe the adjustment variables or the exact contrast direction. This limits evaluation of precision and independent reproduction. The simple recalculation differs from the sponsor analysis; the sponsor’s analysis takes precedence, but the record does not explain the discrepancy.

The record also does not report a detailed statistical analysis plan, multiplicity procedures for secondary outcomes, original sample-size justification, or interim-analysis details. The reported safety counts lack event terms and attribution information. These omissions should be treated as limits of what the registry record reports, rather than as proof that the corresponding procedures or information did not exist.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Promoting Physical Activity in Churchgoing Latinas — NCT01776632.
• Registry record last updated 2021-09-29; status last verified 2021-09.
• Results first posted 2019-04-16.
• 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

NCT01776632, “Promoting Physical Activity in Churchgoing Latinas,” is a completed, randomized, double-masked, parallel-group behavioral trial sponsored by San Diego State University. The registry lists enrollment of 436 and states that 16 churches were randomly assigned to a multilevel physical activity intervention or an attention-control program on cancer screening and prevention.

The primary outcome was accelerometer-based MVPA in minutes per week, described as change from baseline and reported at month 12. The sponsor reported a generalized linear mixed effects analysis with an adjusted mean difference of 0.15 and p = .03. A simple unadjusted recalculation gives a mean difference of -14.5 minutes/week, with a confidence interval from -39.35 to 10.35 and p = 0.253. The registry identifies a discrepancy, so the sponsor’s own analysis takes precedence.

BMI and waist circumference were listed as secondary outcomes. The record reports exclusions from the primary analysis for invalid accelerometer data, but does not describe a complete missing-data strategy or provide full model details. The trial began on 2011-05-11 and had primary completion on 2015-12-21.