Public Messaging to Increase Treatment Seeking for Veterans at Risk for Suicide: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Public Messaging to Increase Treatment Seeking for Veterans at Risk for Suicide (NCT04784663), a randomized na study. The primary outcome is Treatment Initiation.

2. Clinical Question

The study addresses a behavioral and public-health question: whether public messaging can encourage treatment seeking among Veterans whom the registry characterizes as at risk for suicide and resistant to seeking mental health care. It does not test a clinical treatment for suicide risk. The posted primary result is a comparison of participants recorded as initiating treatment in the message-exposure and wait-list control groups.

The registry reports 34 participants with treatment initiation among 229 in the Message Exposure group and 19 among 232 in the Wait List Control group. Its comparison estimates a risk difference of 0.067, with a confidence interval from 0.009 to 0.125. These results describe the recorded outcome in the study groups; they do not, on their own, establish how messaging might perform in other populations or settings.

3. Trial Design

NCT04784663 is listed as a randomized, unmasked, crossover study. The registry lists the study phase as NA and the status as completed. The sponsor is the VA Office of Research and Development. The recorded study start is 2022-12-01, and the primary completion date is 2025-06-30. Enrollment is listed as 355.

The intervention is behavioral messaging, compared with a wait-list control. The immediate-exposure arm description says participants completed baseline assessment and were randomly assigned to receive 4 study videos over the first month. The exposure period ended before telephone-based assessments at 1- and 2-month follow-up. The description is truncated after explaining that videos were delivered by the study’s mobile platform, so fuller delivery details are not reported in the registry record.

The registry also describes wait-list participants who received weekly push notifications while waiting for messages. It identifies wait-list message exposure at T2 and at T3, indicating different timing of exposure. The study is classified as crossover, and the primary-outcome population description notes that exposure was time-varying for an arm: participants contributed control observations while unexposed and intervention observations after exposure. This means that the group labels do not necessarily represent a simple, fixed exposure status across the whole follow-up period.

The registry reports distinct participant counts in the primary-outcome comparison: 229 for Message Exposure and 232 for Wait List Control, alongside total enrollment of 355. The record does not fully explain the relationship between these counts, the crossover timing, and the enrolled population. The interpretation should therefore follow the posted outcome definitions and comparison rather than assuming that each participant contributed to only one fixed group throughout follow-up.

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.

Baseline (T1)

1-month Follow-up (T2)

Reasons for not completing this period:

2 Month Follow-up (T3)

Reasons for not completing this period:

Analysis

Analysis population for the primary outcome, as defined in the registry: The Ns are distinct; Participants exposed at T2 contribute data as control and intervention depending on timing and outcome status (exposure is time-varying for this arm). Participants in this arm contributed data as controls (unexposed) for T1 and T2 until they received the intervention. Participants that had already experienced the outcome prior to crossover continued to contribute data as controls, whereas those who had not yet experienced the outcome were intervention observations for T3.

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 Treatment Initiation, measured over baseline through 2-month follow-up.

The primary endpoint is Treatment Initiation, reported as a count of participants. The registry defines a participant as having initiated treatment if they answered yes to initiating psychological treatment and/or medication or pharmacological treatment in the past month to treat mental health issues. The stated timeframe is baseline through 2-month follow-up.

This endpoint captures a reported behavior rather than a belief, intention, or perception. That distinction matters because the study’s aim is to develop and test public messaging to increase treatment seeking. A question about whether participants started care is more directly connected to that aim than a question about whether they approve of treatment or intend to seek it. The registry also lists secondary measures concerning beliefs about treatment, intentions to seek treatment, perceived barriers, and normative beliefs about seeking mental health care.

The outcome is binary at the participant level: the registry records whether treatment initiation was reported. The posted summary gives event counts and participant denominators for each comparison group. The registry does not report fuller details of how treatment initiation was elicited, verified, or handled when information was unavailable. It also does not provide a detailed account of how repeated assessments were combined into the primary outcome across the full baseline-to-follow-up period.

7. Results Posted in the Registry

• Message Exposure: 14.8% (34/229) versus 8.2% (19/232) on control; risk difference 6.7 percentage points (95% CI 0.9 to 12.5), risk ratio 1.81 (1.07–3.08); unadjusted two-proportion z-test p = 0.025.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is classified according to whether treatment initiation was reported. The registry posts counts and denominators for Message Exposure and Wait List Control, along with group risks and comparative effect estimates. The principal absolute-scale estimate is the risk difference, accompanied by a confidence interval and an unadjusted p-value.

What does a risk difference describe?

In general, a risk difference subtracts one group’s probability of an event from the other group’s probability. It measures an absolute separation on the probability scale. Here, the registry reports a risk difference of 0.067, with a confidence interval from 0.009 to 0.125. The posted group risks are 0.148 for Message Exposure and 0.082 for Wait List Control. The positive risk-difference estimate corresponds to a higher reported risk in the message-exposure comparison group.

The risk ratio and odds ratio provide relative-scale comparisons. In general, a risk ratio divides one group’s risk by the other group’s risk. An odds ratio compares event odds rather than risks. Their interpretation differs from the risk difference, especially when readers want to understand absolute group separation. The registry reports a risk ratio of 1.813, with limits 1.066 and 3.083, and an odds ratio of 1.955, with limits 1.079 and 3.541. These measures are supplemental descriptions of the same posted comparison, not separate outcomes.

How should the confidence interval and p-value be read?

In general, a confidence interval describes uncertainty around an estimate under the assumptions of the statistical procedure. It is not a guarantee that the true effect lies in the interval, and it does not account automatically for limitations that are absent from the model. The interval for the risk difference runs from 0.009 to 0.125. The unadjusted p-value is 0.025. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, nor does it describe the clinical or practical importance of the estimate.

The posted comparison is described as randomized, but the study is also classified as crossover. The primary-outcome description says exposure is time-varying for an arm and that participants can contribute data as controls before receiving the intervention and as exposed afterward. In general, repeated observations and changing exposure status can affect which observations belong in a comparison and how their dependence should be handled. The registry does not report the statistical model, the method used to account for repeated measurements, or the exact approach to exposure timing. That missing detail limits independent assessment of whether the reported uncertainty fully reflects the study structure.

What is not specified about the analysis?

The registry lists zero analyses while also posting a comparison summary for the primary outcome. It does not report a fuller statistical analysis plan, adjustment variables, the handling of missing outcome data, or a prespecified primary contrast beyond the posted comparison. It is therefore not possible to determine from the record whether the reported estimates were adjusted, how all follow-up observations were combined, or which analysis population was used. Those elements matter for interpreting a randomized crossover study, particularly when exposure changes over time.

The registry lists 5 outcome measures and 4 posted secondary outcomes. In general, testing multiple outcomes or contrasts raises a multiplicity question: if many hypotheses are assessed, the chance of at least one apparently unusual result can increase. Whether any adjustment or hierarchy was planned or used is not reported in the registry record. The unadjusted p-value should therefore be read as the value attached to the posted comparison, not as evidence that multiplicity was addressed.

For a count-based binary outcome, the event count and denominator are essential context. The primary results report 34 of 229 and 19 of 232. The total enrollment is 355, and the record describes distinct Ns and time-varying exposure. Those figures should not be combined or treated as a simple accounting of unique participants without further information. The registry does not provide enough detail to reconstruct the participant flow or reproduce the full analysis from the posted summary alone.

General statistical interpretation also distinguishes an estimate from the procedure used to estimate it. A confidence interval can express sampling uncertainty under a model, while design features, missing data, measurement error, and analysis choices can introduce additional uncertainty not represented by that interval. The posted estimates are useful descriptions of the registered comparison, but a more complete methods report would be needed to evaluate all assumptions.

10. Confidence Intervals and Precision

The confidence interval for the risk difference extends from 0.009 to 0.125 around the estimate of 0.067. This interval communicates that the data are compatible with a range of group differences under the method used. It is not a single exact value for the underlying effect. The interval’s lower limit is close to zero in absolute terms, while its upper limit is farther from zero, so the estimate should not be read as precisely pinning down the size of the difference.

In general, a confidence interval reflects sampling uncertainty conditional on the statistical model and assumptions. It does not automatically account for uncertainty from unreported analysis choices, missing outcomes, or possible measurement limitations. The registry does not describe the model used for the crossover and time-varying exposure structure, so the interval cannot be independently assessed against those design features.

The registry also gives intervals for relative measures: the risk ratio is 1.813, with limits 1.066 and 3.083, and the odds ratio is 1.955, with limits 1.079 and 3.541. These intervals express uncertainty on different scales from the risk-difference interval. Their values should be interpreted according to the measure named, rather than as absolute changes in treatment initiation.

The p-value of 0.025 is unadjusted. A p-value and confidence interval answer related but different questions: the interval shows a range of effect estimates compatible with the data and procedure, while the p-value quantifies compatibility with a specified null under an analysis model. Neither replaces consideration of precision, study design, or the practical meaning of the measured outcome.

11. 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 event counts. They illustrate the sample sizes that would be needed under the stated assumptions to detect a chosen fraction of the observed effect. For 100% of the observed effect, the entries are 360 participants per arm for 80% power and 482 participants per arm for 90% power. For 75% of the observed effect, they are 600 per arm for 80% power and 803 per arm for 90% power. For 50% of the observed effect, they are 1,258 per arm for 80% power and 1,683 per arm for 90% power.

In general, power is the chance that a study would meet its stated statistical decision rule if a particular effect were present and the assumptions held. The 80% and 90% columns describe different target chances of detecting the assumed effect. A higher target power requires more participants under the same assumptions. Smaller effects also require more participants to detect, which is reflected by the larger figures for smaller fractions of the observed effect.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. These are planning assumptions for the illustration, not the original trial’s design assumptions. The trial’s own sample-size justification is not reported in the registry record. This is not observed power: the figures are prospective planning illustrations based on an observed estimate, not a measure of how powerful the completed trial turned out to be.

In general, a sample-size curve visualizes how the planned participant requirement changes as the assumed effect changes. Its interpretation remains conditional on the planning assumptions and the effect used as a reference. It does not show that a future study will obtain the same effect or that the observed comparison is free of uncertainty.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.082; treatment proportion p₁ = 0.148; average p̄ = 0.115.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4515 = 0.8849.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4490 = 0.3779.
4. n = (0.8849 + 0.3779)² / (0.0666)² = 359.8, rounded up to 360 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0818965517241379                          # control proportion
p1 <- 0.148471615720524                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4784663)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 360 (80% power), 482 (90% power)
 75% of observed effect: n per arm = 600 (80% power), 803 (90% power)
 50% of observed effect: n per arm = 1,258 (80% power), 1,683 (90% power)
power.prop.test: 359.8 
Simulated power at n = 360 per arm: 0.809 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists 5 outcome measures, including the primary endpoint and 4 secondary outcomes: mean change in beliefs about mental health treatment, intentions to seek treatment, perceived treatment barriers, and normative beliefs about seeking mental health care. Considering multiple outcomes can raise multiplicity concerns. In general, when several hypotheses are tested, the chance of at least one result appearing statistically notable can increase. The registry does not report whether the outcomes were arranged in a testing hierarchy or whether any adjustment for multiplicity was planned or performed.

The displayed primary comparison has an unadjusted p-value of 0.025. No adjusted p-value or multiplicity procedure is reported in the registry record. Consequently, the posted p-value should be understood as unadjusted, and the registry does not establish how it should be interpreted in relation to the secondary outcomes or any additional comparisons.

Missing-data procedures are also not reported in the registry record. The record does not state how participants without a follow-up assessment were handled, whether outcome data were imputed, or whether the analysis used only participants with observed outcomes. It also does not report a detailed participant-flow account connecting enrollment of 355 with the primary comparison denominators of 229 and 232.

The primary-outcome description notes that Ns are distinct and that participants exposed at T2 can contribute data as control and intervention depending on timing and outcome status. It also says exposure is time-varying for an arm. The statistical method used to accommodate that arrangement, including how repeated assessments were handled, is not reported in the registry record.

The registry lists zero analyses while posting the outcome comparison. It does not identify a full analysis population, such as a named intention-to-treat or per-protocol population, and does not specify whether estimates were adjusted for other variables. These omissions do not invalidate the posted summary, but they make it difficult to assess the analysis choices and reproduce the comparison independently.

14. 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 serious adverse event figures are reported separately for Message Exposure and Wait List Control. The registry records 0 serious adverse events among 229 at risk in Message Exposure and 0 among 232 at risk in Wait List Control. It also reports 0 other adverse events in each group and 0 deaths in each group.

These figures describe events recorded in the registry for the stated groups and denominators. A zero count means no event of that category was recorded in the posted results; it does not establish that no event occurred outside the reporting process or that an intervention has no safety concerns. The registry does not provide serious-event terms, and the serious-event terms list is empty.

The adverse-event counts should be read separately from the primary treatment-initiation outcome. They do not provide information about whether participants initiated treatment, nor do they resolve the uncertainties in the primary analysis. The registry does not report further detail about event definitions, collection procedures, follow-up completeness, or the methods used to assess adverse events.

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

The result shows a higher recorded treatment-initiation risk in the Message Exposure group than in the Wait List Control group in the posted comparison. The estimate is a risk difference of 0.067, with a confidence interval from 0.009 to 0.125 and an unadjusted p-value of 0.025. The registry also reports 34 treatment initiations among 229 in Message Exposure and 19 among 232 in Wait List Control.

This is a result about a specified behavioral outcome during baseline through 2-month follow-up. The endpoint records whether participants reported initiating psychological treatment and/or medication treatment in the past month for mental health issues. It does not measure the quality, duration, or clinical effect of any treatment, and it does not directly measure suicide attempts, suicide deaths, or longer-term health outcomes.

The study’s aim is to develop and test public messaging for Veterans at risk for suicide who are resistant to seeking mental health care following separation from military service. The posted comparison is relevant to that question, but it does not by itself establish that the messages would produce the same result in other populations, communication settings, or periods of follow-up. Nor does it show which message content was responsible for the group difference.

The study is randomized and classified as crossover, with exposure changing over time for at least part of the population description. The registry does not report the analysis model or how the crossover timing and repeated observations were incorporated. The reported estimate should therefore be interpreted as the result of the posted analysis, with caution about the unreported analysis details.

In general, statistical evidence of a difference is not the same as proof of a particular mechanism or a complete account of practical importance. The confidence interval conveys uncertainty about the estimate under the analysis used; missing methodological details and missing-data procedures are separate considerations. The registry result supports a description of the recorded comparison, not a broad claim about treatment effectiveness or clinical benefit.

16. Why This Trial Matters Statistically

This study’s statistical challenge is not only comparing event counts. It combines randomized assignment with a crossover structure and exposure that can change over time. The primary-outcome description explicitly says participants may contribute control observations before receiving messages and intervention observations after exposure. That makes the definition of the comparison and the handling of repeated observations important to interpreting the estimate and its uncertainty.

The endpoint also connects a communication intervention to a behavioral outcome. The registry distinguishes treatment initiation from beliefs, intentions, perceived barriers, and normative beliefs, which are listed as secondary outcomes. Separating those outcomes is statistically and conceptually useful: a change in an attitude or intention is not identical to reporting that treatment was initiated.

The posted risk difference and confidence interval offer an absolute-scale description of the primary comparison, while the risk ratio and odds ratio provide relative-scale descriptions. Reporting more than one scale can help readers see that effect measures answer different interpretive questions. The interval also emphasizes that the point estimate is not the only plausible value under the analysis.

The registry record leaves important analytic details unreported, including the model, missing-data handling, multiplicity procedures, and analysis population. Those omissions matter because the primary result is accompanied by multiple listed outcomes and because the crossover design creates timing and dependence questions. A clear statistical analysis plan and transparent participant-flow reporting would help readers understand how the displayed estimates relate to the design.

Finally, the planning illustration demonstrates how sample-size requirements depend on the assumed effect and target power. Its figures are not the trial’s original design justification and are not observed power. Keeping that distinction clear prevents a planning calculation based on the observed estimate from being mistaken for evidence that the completed study was adequately powered.

17. 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 primary comparison involves a crossover design, and the registry describes exposure as time-varying for an arm. Participants can contribute data while unexposed and later after receiving the intervention. The record does not report the model used to account for this timing, repeated observations, or any dependence between observations from the same participant. That limits assessment of how directly the reported confidence interval reflects the design.

The enrollment count is 355, while the primary-outcome comparison lists 229 and 232 as group denominators and describes the Ns as distinct. The registry does not provide a complete participant-flow explanation linking those figures. The denominators should therefore be treated as the posted comparison counts, not assumed to represent mutually exclusive sets of unique participants across the entire study.

The outcome is based on reported treatment initiation during the stated timeframe. The registry does not describe verification procedures, detailed question wording beyond the definition, or how repeated responses were combined. The record also does not report missing-data handling, follow-up completeness, or a named analysis population.

The registry lists zero analyses but posts a primary comparison, and it does not report a full statistical analysis plan, adjustment variables, or multiplicity procedures for the primary and secondary outcomes. The listed sample-size figures are planning illustrations based on the observed effect rather than the trial’s documented original design assumptions; the original sample-size justification is not reported in the registry record.

Finally, the registry’s arm descriptions are incomplete, and the message-delivery details are not fully reported. This limits assessment of intervention fidelity and the precise contrast between immediate message exposure and wait-list timing. These limitations concern interpretation of the posted result; they do not change the counts and estimates recorded for the comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Public Messaging to Increase Treatment Seeking for Veterans at Risk for Suicide — NCT04784663.
• Registry record last updated 2026-07-09; status last verified 2026-06.
• Results first posted 2026-07-09.
• 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.

21. Record Summary

NCT04784663 is a completed randomized, unmasked crossover study of public messaging intended to increase treatment seeking among Veterans at risk for suicide and resistant to seeking mental health care after separation from military service. The registry lists enrollment of 355, with study dates from 2022-12-01 to primary completion on 2025-06-30. The sponsor is the VA Office of Research and Development.

The primary endpoint is participant-reported initiation of psychological treatment and/or medication treatment in the past month for mental health issues, assessed over baseline through 2-month follow-up. The posted comparison reports 34 of 229 participants in Message Exposure and 19 of 232 in Wait List Control, with a risk difference of 0.067 and a confidence interval from 0.009 to 0.125. The unadjusted p-value is 0.025.

The registry also lists 4 secondary outcomes. Analysis details, missing-data procedures, multiplicity handling, and the original sample-size justification are not reported in the registry record. The design’s crossover timing and time-varying exposure are important context for reading the posted estimates.