Text Message Intervention for Alcohol Use and Sexual Violence in College Students: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Text Message Intervention for Alcohol Use and Sexual Violence in College Students (NCT05065918), a randomized na study. The primary outcome is Number of Drinking Days Per Month.

2. Clinical Question

The comparison is between two forms of text-message content, not between receiving messages and receiving no content. This matters when interpreting the contrast: the data address the difference between the alcohol-use reduction content and the combined alcohol-use and sexual-violence harm-reduction content. The registry record does not describe a no-message or usual-practice arm.

The primary endpoint is a continuous count of drinking days over the stated recall period. The reported results therefore concern the mean number of days, rather than the number of drinks, binge-drinking episodes, or the proportion of students who drank. Those other outcomes are not the primary measure reported in this record.

The record marks the trial completed and lists enrollment of 183. It does not report a more detailed primary population definition or explain whether the endpoint analysis included every enrolled participant. That information is relevant when deciding exactly to whom the reported comparison applies.

3. Trial Design

The registry record describes a randomized, parallel-group study with no masking. Enrollment was 183. Participants were assigned to one of two behavioral-content arms: alcohol use reduction content, or sexual violence and alcohol use harm reduction content. Both arms are described in terms of text-message content. The record does not provide further detail about how the messages were delivered or how long participants received them.

The study is described as a pilot. Its brief summary states that it was designed to pilot a text-message behavior change intervention aimed at decreasing binge drinking and increasing the use of sexual-violence harm reduction strategies among college students. The primary outcome posted for the trial is narrower than that broad aim: mean number of drinking days in the past 30 days at 3 month follow up. A change in this endpoint would not by itself establish a change in every intended behavior or in sexual-violence harm reduction strategies.

The registry lists the primary endpoint as a mean with standard deviation, assessed at 3 month follow up using a 30-day timeline follow-back. The posted arm summaries include 92 participants in control and 91 in intervention. These are the sample sizes associated with the primary outcome summaries; whether they are the full randomized groups or an analysis subset is not reported in the registry record.

The record lists secondary outcomes concerning knowledge of sexual violence and alcohol risk and self-efficacy to obtain sexual consent. Each title appears twice in the secondary-outcome list, while the posted results include results for the two named measures. The record lists 10 outcome measures and 10 analyses overall, but does not give a complete account of all measures or analyses in the posted results.

The study is listed as completed, with start date 2021-11-04 and primary completion date 2023-08-31. Phase is listed as NA. Further protocol details—including original sample-size assumptions, allocation procedures beyond randomized assignment, and the intended statistical analysis plan—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.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Drinking Days Per Month, measured over 3 month follow up.

The primary endpoint is the mean number of drinking days in the past 30 days at 3 month follow up. It is measured with a 30-day timeline follow-back, a structured recall approach that asks participants to report behavior over a specified recent period. In this study, the unit is drinking days, not drinks consumed or episodes meeting a binge-drinking definition.

A continuous mean summarizes the average reported number of drinking days in each arm. The posted control mean was 6.45, with standard deviation 4.5, among 92 participants. The intervention mean was 5.91, with standard deviation 4.97, among 91 participants. The recalculated unadjusted mean difference, intervention compared with control, was -0.54; its 95% confidence interval was -1.914 to 0.834.

This endpoint is relevant to the stated aim of reducing alcohol use because it records how many days participants drank during the recall period. It does not measure all dimensions of alcohol use. In particular, the endpoint alone does not quantify the amount consumed on drinking days, identify binge-drinking episodes, or measure use of sexual-violence harm reduction strategies.

The registry record does not report additional details about the measure’s scoring beyond the timeline follow-back description, nor does it describe missing-response handling or the population included in the endpoint analysis. The results therefore describe the posted means and comparison at follow up, while those unreported details limit assessment of how the endpoint data were collected and analyzed.

7. Results Posted in the Registry

• Intervention - Sexual Violence and Alcohol Use Harm Reduction Content: mean 5.91 versus 6.45 on control; difference -0.54 (95% CI -1.91 to 0.83), standardized effect d = -0.11; z-test p = 0.441.

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.

Knowledge of Sexual Violence and Alcohol Risk

• 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:
  • Intervention - Sexual Violence and Alcohol Use Harm Reduction Content: mean 36.72 versus 37.35 on control; difference -0.63 (95% CI -1.74 to 0.48), standardized effect d = -0.16; z-test p = 0.267.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention - Sexual Violence and Alcohol Use Harm Reduction Content and the control. The interval gives the range of effects that remain compatible with the data.

Self-efficacy to Obtain Sexual Consent.

• 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:
  • Intervention - Sexual Violence and Alcohol Use Harm Reduction Content: mean 40.92 versus 42.78 on control; difference -1.86 (95% CI -4.00 to 0.28), standardized effect d = -0.25; z-test p = 0.089.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention - Sexual Violence and Alcohol Use Harm Reduction Content and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes concern knowledge of sexual violence and alcohol risk and self-efficacy to obtain sexual consent. The arm summaries and sponsor analyses do not form a uniform pattern of evidence across these measures. The registry record lists the two outcome titles twice in its secondary-outcome list, while results are posted for the two named measures.

The secondary outcomes address concepts closer to the intervention’s sexual-violence harm-reduction aim than the primary drinking-days endpoint does. They are not substitutes for the primary endpoint: knowledge and self-efficacy scores do not directly measure drinking frequency or actual use of harm reduction strategies. The primary finding is therefore interpreted on its own outcome scale, with secondary outcomes offering separate, related information.

Secondary results generally carry less weight than a prespecified primary result when many outcomes or comparisons are examined. Each additional test creates more opportunity for an apparently notable result to arise by chance. This is the general statistical concern known as multiplicity. The registry record does not report whether a multiplicity adjustment or a hierarchy for secondary testing was used. The reported secondary p-values should therefore be treated as unadjusted evidence unless the record documents otherwise.

The record lists 10 outcome measures and 10 analyses overall, but the full set of measures and analysis details is not described in the posted results. This limits the ability to judge how selectively the displayed secondary results represent all analyses. No unreported outcomes or estimates should be inferred from the count alone.

In combination, the secondary outcomes can help characterize what was measured beyond drinking days, but they do not establish a broad intervention effect by themselves. Their interpretation depends on the scoring, coding, prespecification, missing-data handling, and multiplicity procedures, several of which are not reported in the registry record.

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

• Knowledge of Sexual Violence and Alcohol Risk
• Knowledge of Sexual Violence and Alcohol Risk
• Self-efficacy to Obtain Sexual Consent.
• Self-efficacy to Obtain Sexual Consent.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s reported number of drinking days is summarized as a mean within each arm. A standard deviation describes how spread out individual measurements were around an arm’s mean. It is not the uncertainty interval for the difference between arms. The control standard deviation was 4.5 and the intervention standard deviation was 4.97, indicating that individual responses varied around their respective means.

What does the mean difference represent?

The unadjusted mean difference compares the intervention mean with the control mean. A negative estimate means the intervention arm’s observed mean was lower. The recalculated estimate was -0.54 drinking days. This is a contrast between arm averages at follow up; it is not a within-person change from baseline. No baseline value for this outcome is included in the posted primary results.

The recalculated comparison uses the posted group means and variation as a simple, unadjusted comparison. It does not use a regression adjustment for other variables. The registry separately reports a linear regression with a slope estimate. Because the record does not give the model’s covariates, coding details, or other specification, the regression result should be described as reported rather than treated as an exact duplicate of the unadjusted calculation.

How should the confidence interval be read?

A confidence interval expresses the range of effect estimates reasonably compatible with the observed data under the method’s assumptions. The primary unadjusted 95% interval is -1.914 to 0.834 drinking days. Since the interval includes zero, the data are compatible with no difference as well as with differences in either direction. The interval’s endpoints are not guaranteed limits for the true effect; they communicate sampling uncertainty.

The p-value is another summary of compatibility between the data and a specified null model. The unadjusted p-value was 0.441, and the registry regression p-value was 0.448. These values do not describe the probability that the null hypothesis is true, nor do they measure the probability that the result will reproduce. They should be interpreted alongside the effect estimate and its interval, rather than as a stand-alone measure of importance.

Why report the standard deviation?

Variation among participants affects how precisely an arm mean and an arm difference can be estimated. When observations vary substantially, a given sample size generally yields less precision than it would if observations were more tightly clustered. This is a general statistical principle. In the primary result, the arm standard deviations are 4.5 and 4.97, while the estimated pooled standard deviation used in the recalculation is 4.74.

Over-dispersion is a general concern when count data vary more than a model’s assumed distribution allows. If that occurs, standard errors from a model that assumes too little variation can be too small, leading to overly narrow intervals and misleading tests. The primary result is reported as a mean and standard deviation, with a linear-regression analysis also reported. The registry record does not report a count-distribution model, an over-dispersion assessment, or diagnostics, so no claim can be made about whether over-dispersion was evaluated.

What does a standardized effect add?

A standardized mean difference expresses a mean contrast relative to a measure of spread, allowing outcomes recorded on different scales to be described on a common scale. For the primary outcome, the recalculated standardized effect was -0.114. This is a descriptive scale-free summary, not a separate outcome and not a statement of clinical importance. The record does not report a threshold for what would count as a meaningful difference in drinking days.

Such standardized effects depend on the variability used in the calculation. They are useful for interpreting planning illustrations, but they can be less directly interpretable than the original-unit estimate. The original-unit estimate and its interval remain important because they retain the drinking-days scale used by the study.

What is the role of randomization?

Randomized assignment is intended to make groups comparable on average with respect to measured and unmeasured characteristics, subject to the trial’s implementation and the effects of chance. The record states that allocation was randomized and that masking was none. It does not describe the randomization sequence, concealment procedures, or whether participants and outcome assessors knew the assigned content. Those details are not reported in the registry record.

Randomization does not guarantee identical group characteristics in a particular trial, especially in a pilot. Nor does it resolve issues such as incomplete outcome data or deviations from assigned content. The record does not report the analysis population, adherence, or missing-data approach. These are therefore relevant areas of uncertainty when interpreting the statistical comparison.

What does the regression result tell us?

The registry identifies the reported method as linear regression and the parameter as a slope. For the primary endpoint, the reported slope was -0.536, with a 95% confidence interval from -1.929 to 0.857 and p = 0.448. The estimate resembles the unadjusted difference, but the record does not describe whether the model included any additional terms. It would be inappropriate to infer adjustment for baseline values or other covariates from the method name alone.

For a regression estimate, interpretation depends on how treatment assignment and the outcome are coded and on which terms are included. The record names the groups and provides the slope, but does not spell out those details. The reported estimate and interval can still be quoted as the registry analysis, while caution is warranted about attributing features to the model that the record does not describe.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated difference. The primary recalculated mean difference was -0.54 drinking days, with a 95% confidence interval from -1.914 to 0.834. The interval spans zero and includes estimates in both directions. Thus, the observed estimate alone should not be read as a precise determination that the intervention arm had fewer drinking days.

The registry’s own estimate was -0.536, with a 95% confidence interval from -1.929 to 0.857. Its interval also covers zero and is similar in overall range to the unadjusted interval. The two intervals reflect uncertainty in their respective analyses; they do not represent a range containing a fixed proportion of individual participants’ outcomes.

The interval’s width is influenced by the amount of variation in reported drinking days and the number of participants contributing data. The posted primary summaries list 92 participants in control and 91 in intervention, with standard deviations of 4.5 and 4.97. The record does not report the number randomized to each arm separately from the outcome sample sizes or explain whether there were missing endpoint observations.

Confidence intervals do not describe the probability that a particular effect lies inside the displayed interval. Rather, under the assumptions of the method, the procedure used to form such intervals has a stated long-run coverage property. In practical reading, the main point is that a wide interval indicates limited precision and that the primary interval leaves room for differences in either direction.

The registry does not report a threshold for a clinically or behaviorally important difference. Statistical uncertainty and substantive importance are distinct: an interval can be evaluated for precision, but deciding what range would matter requires a meaningful benchmark that is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s design justification. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario targets an effect that is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

For these continuous outcomes, the figures are participants per arm, not total participants across both arms and not total events. The 80% power column indicates the number of participants per arm estimated to give an 80% chance of detecting the scenario effect if that effect and the planning assumptions were correct. The 90% power column expresses the corresponding planning target for a 90% chance. These are prospective design concepts, not guarantees for a future study.

Planning for 100% of the observed primary effect gives 1,210 participants per arm for 80% power and 1,619 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,150 participants per arm for 80% power and 2,878 participants per arm for 90% power. Planning for 50% of the observed effect gives 4,838 participants per arm for 80% power and 6,476 participants per arm for 90% power.

The pattern reflects a general principle: smaller effects are harder to distinguish from random variation, so detecting them at the same power generally requires more participants. Increasing the target power also requires a larger planned sample under the same assumptions. Because these calculations use an effect observed in a pilot, they should be treated as planning illustrations rather than as evidence that the pilot had, or lacked, a particular probability of success. This is not observed power.

The figures depend on the assumptions used. They do not account for any design features or analysis choices that are not included in the stated planning method. The registry record does not report whether the trial’s actual planning used these assumptions or whether it used another approach.

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 = -0.540; pooled standard deviation σ = 4.740.
2. n = 2 × (1.96 + 0.842)² × 4.740² / -0.540² = 1,209.3, rounded up to 1,210 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 <- -0.54                      # observed difference in means
sigma <- 4.73953106289352                     # 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(5065918)
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 = 1,210 (80% power), 1,619 (90% power)
 75% of observed effect: n per arm = 2,150 (80% power), 2,878 (90% power)
 50% of observed effect: n per arm = 4,838 (80% power), 6,476 (90% power)
power.t.test: 1210.2 
Simulated power at n = 1,210 per arm: 0.800 (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 registry’s primary analysis is a linear regression, reported as a slope of -0.536. Its 95% confidence interval is -1.929 to 0.857 and its p-value is 0.448. The unadjusted recalculation from the posted arm means estimates a mean difference of -0.54, with a 95% confidence interval from -1.914 to 0.834 and p = 0.441.

The central estimates and overall uncertainty are similar: both analyses give a negative point estimate and intervals that include zero. The values are not identical, as can occur when a model-based analysis and an unadjusted summary-statistic calculation use different formulations or precision. The record does not provide enough detail to identify the reason for the small numerical differences, so no specific explanation should be assumed.

The discrepancy flag is false. The registry’s own analysis is therefore presented as reported, alongside the transparent unadjusted recalculation. The recalculation is not a replacement for the sponsor’s analysis and does not incorporate any regression specification that may have been used. Conversely, the registry record does not describe enough model detail to evaluate adjustments or assumptions beyond identifying linear regression.

For interpretation, both sources of evidence point to a similar estimate with substantial uncertainty around the contrast. The registry estimate should be treated as the reported trial analysis; the recalculated result helps readers understand the simple difference between the posted arm means.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, groups, or analytic choices are tested. Even if each test is evaluated at the same nominal significance threshold, considering more tests increases the chance that at least one result will appear unusual under a no-effect scenario. This is a general statistical issue, not a claim that any particular reported result is false.

The registry record lists 10 outcome measures and 10 analyses. It also identifies secondary outcomes relating to knowledge of sexual violence and alcohol risk and self-efficacy to obtain sexual consent. The record does not report a family-wise error adjustment, false-discovery procedure, testing hierarchy, or other multiplicity plan. The secondary findings should consequently be read as exploratory or otherwise unadjusted unless a separate analysis plan establishes a different status.

Missing data are another important part of interpreting trial estimates. The posted outcome summaries list 92 participants in control and 91 in intervention for the primary outcome. The record does not report how many participants were randomized to each arm, how many missed follow up, why any observations might be absent, or how missing values were handled. It also does not state whether the results use an intention-to-treat population, a complete-case population, or another analysis set. Those details are not reported in the registry record.

Without these details, it is not possible to assess from the registry entry whether missingness could have affected the arm comparison or whether the analysis retained all randomized participants. This is a limitation of what can be evaluated, not evidence that missing data occurred or that a particular method was used.

The record identifies randomization and no masking, but further information on allocation concealment, adherence, departures from assigned content, and outcome assessment procedures is not reported. These design and analysis details matter because they help readers judge the reliability of an estimate and the possibility of bias. Their absence from the registry record should be kept distinct from evidence that any specific bias occurred.

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.

For serious adverse events, the registry lists 0 affected participants among 92 at risk in the control arm and 0 among 91 at risk in the intervention arm. Deaths are listed as 0 in each arm. The record lists 0 affected participants for other adverse events as well, among the same respective numbers at risk.

These figures mean that no affected participants or deaths are recorded in the posted adverse-event summaries for either arm. They do not establish that no event of any kind occurred outside the scope or reporting practices represented in the registry entry. The record does not provide serious-event terms, and no top serious-event terms are listed.

With relatively small arm counts, zero recorded events cannot rule out uncommon harms. More generally, absence of reported events is not proof of absence of risk. The registry record does not describe the adverse-event collection period or definitions beyond the serious and other adverse-event categories, so the figures should be interpreted as registry reporting rather than as a complete characterization of every possible safety outcome.

These summaries are separate from the primary efficacy endpoint and do not change how its mean difference or confidence interval should be interpreted.

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

The primary result describes the mean number of drinking days in the past 30 days at 3 month follow up among participants in two text-message content arms. The intervention arm’s posted mean was 5.91 and the control arm’s was 6.45. The unadjusted comparison was -0.54 drinking days, and its 95% confidence interval ranged from -1.914 to 0.834. The interval includes zero, so the result leaves uncertainty about the direction and size of the difference.

This is not a direct test of every goal named in the study summary. The primary endpoint does not measure binge-drinking episodes, amount consumed, or use of sexual-violence harm reduction strategies. The posted secondary measures address knowledge and self-efficacy, but those measures do not directly establish changes in behavior or experiences of sexual violence.

The result also does not compare the combined intervention with no text messages. The control arm received alcohol use reduction content, so the estimate concerns the relative difference between two content approaches. No conclusion about the effect of receiving messages versus receiving none follows from this comparison.

The confidence interval reflects statistical uncertainty, not the full range of possible limitations. Missing-data procedures, analysis populations, and detailed regression specifications are not reported in the registry record. These gaps limit evaluation of how sensitive the estimates may be to analytic choices or incomplete follow-up.

Because this is described as a pilot, its findings are best understood as estimates from a limited study intended to test an intervention approach, not as a final determination of its effects. The posted results neither establish that the approaches are equivalent nor demonstrate a clear difference in the primary endpoint. They identify an observed contrast and the uncertainty associated with it.

No treatment recommendation follows from these results. Their meaning is statistical and specific to the populations, message content, outcome definition, and follow-up described in the registry record. Broader conclusions would require evidence that addresses the unreported design details and outcomes relevant to those broader claims.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates why an observed difference and its uncertainty need to be read together. The intervention mean was lower than the control mean at follow up, but the confidence interval for the estimated contrast includes zero and extends in both directions. Focusing only on the point estimate would overstate how clearly the data locate the difference.

It also illustrates the distinction between a pilot’s observed effect and a planned effect for a future study. The planning illustrations use fractions of the observed effect and show that targeting a smaller effect requires more participants per arm under the stated assumptions. These are design calculations, not a retrospective measure of whether the pilot was adequately powered.

The two arms both received behavioral text-message content, so the trial estimates a contrast between content strategies. That is a useful design distinction: the primary result cannot be interpreted as the effect of text messages as a delivery method compared with no messages. The comparison’s scope is defined by the actual control condition.

Finally, the record makes visible the limits of registry reporting. It gives the main outcome summaries and a sponsor analysis, but does not report the original sample-size rationale, missing-data procedures, analysis populations, multiplicity plan, or detailed regression specification. These omissions are not evidence of poor conduct, but they prevent a complete audit of the analysis from the registry entry alone. Statistical interpretation depends on both the estimates and the details needed to understand how they were produced.

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 primary outcome is self-reported drinking frequency over the past 30 days, assessed at 3 month follow up with a timeline follow-back. The registry does not report additional information about validation, administration, or completeness of the measure. Recall and reporting characteristics are therefore relevant considerations, but the record does not establish whether they affected the results.

The endpoint captures drinking days, not amount consumed, binge-drinking frequency, or sexual-violence harm reduction behavior. This limits the conclusions that can be drawn about the broader aims described in the study summary. The secondary measures listed in the record concern knowledge and self-efficacy, which are distinct from behavioral outcomes.

The control arm received alcohol use reduction content, so the study does not provide a comparison against no intervention. The record also states that masking was none. It does not describe who knew assignment or whether outcome assessors were aware of it. The consequences of this design feature cannot be determined from the registry information alone.

The available record does not report baseline outcome values, a detailed regression specification, the analysis population, missing-data procedures, adherence, or deviations from assigned content. The sample-size rationale and multiplicity plan are also not reported. These omissions constrain assessment of the analysis and the strength of secondary findings.

The study is described as a pilot and enrolled 183 participants, with primary outcome summaries for 92 control and 91 intervention participants. Its estimates have appreciable uncertainty, and the planning illustrations based on the observed effect indicate much larger hypothetical per-arm sample sizes under their assumptions. Those illustrations do not remedy the limitations of the observed data or establish the sample size needed under a different true effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Text Message Intervention for Alcohol Use and Sexual Violence in College Students — NCT05065918.
• Registry record last updated 2024-10-17; status last verified 2024-02.
• Results first posted 2024-10-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed randomized, parallel-group pilot enrolled 183 college students and compared alcohol use reduction text-message content with content addressing both alcohol use and sexual-violence harm reduction. Masking is listed as none.

The primary endpoint was mean drinking days in the past 30 days at 3 month follow up, measured with a 30-day timeline follow-back. The posted means were 6.45 in control and 5.91 in intervention. The registry’s linear-regression estimate was -0.536, with a 95% confidence interval from -1.929 to 0.857 and p = 0.448. The unadjusted recalculation was -0.54, with a 95% confidence interval from -1.914 to 0.834 and p = 0.441.

The primary interval includes zero and leaves uncertainty about the direction and size of the contrast. Secondary measures address knowledge and self-efficacy; their interpretation is limited by unreported multiplicity procedures. Missing-data methods, analysis populations, original sample-size assumptions, and detailed model specifications are not reported in the registry record.