Pediatric Inpatient Firearm Safety Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pediatric Inpatient Firearm Safety Study (NCT03077646), a randomized na study. The primary outcome is Change in Likert Scale of Frequency of Asking About Guns in the Home When Their Child Goes to Another Person's Home, Pre-intervention and 1 Month Post-intervention.

2. Clinical Question

The registry frames the study as an evaluation of the inpatient setting as an opportunity to discuss firearm safety with parents or guardians. It also asks whether physician-delivered review adds an effect beyond video and written information alone. The primary measure is a self-reported Likert score about asking before a child goes to another person’s home. That is a specific behavior, not a direct measure of firearm storage, firearm access, or injury.

The intended assessment schedule included measurement immediately after intervention and a 30-day follow-up phone call. The primary outcome description specifies baseline and the last 30 days. The posted primary results are based on paired pre- and post-intervention responses within each group, followed by recalculated, unadjusted comparisons with control. They therefore address reported change in this particular behavior over the specified recall period; they do not, by themselves, establish effects on other firearm-safety practices or on child health outcomes.

3. Trial Design

The registry describes a randomized, parallel-group study with no masking. Its status is completed, and the recorded enrollment is 225. The study dates listed in the record are 2017-03-01 for start and 2019-08-09 for primary completion. The condition is firearm safety, and Montefiore Medical Center is listed as sponsor. The registry lists phase as NA.

Participants were assigned to one of three groups: Be SMART alone, Be SMART with physician review, or control using tobacco-smoke-exposure materials. The first two groups received the same firearm-safety video and handouts; the physician-review group also had a physician review the information using a checklist. The control group watched a video about children and tobacco smoke and received related handouts. The registry’s brief summary describes assessment immediately after intervention and at a 30-day follow-up phone call.

The primary outcome is a within-person change measure. Its analysis population is described as paired samples: responses from the same study subject before and after intervention. The posted primary arm summaries include 25 paired responses for Be SMART alone, 27 for Be SMART plus physician review, and 20 for control. Those are the primary analysis counts, not the enrollment figures. The record does not explain the difference between enrollment and the numbers contributing paired primary responses, so the reasons for the smaller paired analysis samples are not reported in the registry record.

The registry record does not report allocation concealment, the method used to generate the random sequence, or which participants or study staff knew the assigned group. It also does not report the trial’s original sample-size justification or detailed statistical analysis plan. These details matter when assessing how allocation and analysis may have affected the estimates, but they cannot 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.

Before assignment: The parent/guardian only was enrolled (child was not), therefore it is not a dyad.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Limited sample for analysis to paired samples within each group (samples where we have responses from the same study subject pre and post)

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change in Likert Scale of Frequency of Asking About Guns in the Home When Their Child Goes to Another Person's Home, Pre-intervention and 1 Month Post-intervention, measured over Baseline and last 30 days.

The primary endpoint is change in how often a parent or guardian asked whether there were guns in another person’s home when the child went there. The reported recall period is the last 30 days, with assessment at baseline and after intervention. Responses use a five-category Likert scale: 1=never, 2=rarely, 3=sometimes, 4=most of the time, and 5=always. The registry reports the outcome as a mean score with standard deviation.

This endpoint was selected to capture a concrete, self-reported safety-related practice that could plausibly be discussed during an inpatient encounter. A change score allows each participant’s post-intervention response to be considered in relation to that participant’s baseline response. Pairing is useful because it accounts for the fact that the two observations come from the same person rather than treating them as unrelated measurements.

Interpretation is limited to this reported behavior and the scale used. A higher score indicates more frequent asking according to the response categories, but the score does not directly document what happened in a conversation, whether a destination home contained firearms, or whether storage practices changed. The registry does not report validation details for the scale or a threshold defining a meaningful change. These endpoint details are not reported in the registry record.

7. Results Posted in the Registry

• Be SMART Alone: mean 0.80 versus 0.90 on control; difference -0.10 (95% CI -1.01 to 0.81), standardized effect d = -0.06; z-test p = 0.829.
• Be SMART + MD Review: mean 0.60 versus 0.90 on control; difference -0.30 (95% CI -1.09 to 0.49), standardized effect d = -0.22; z-test p = 0.454.

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.

Doctors Who Take Care of Kids Should Talk to Parents About Safe Gun Storage at 1 Month Post-intervention

• 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:
  • Be SMART Alone: mean 4.20 versus 4.30 on control; difference -0.10 (95% CI -0.45 to 0.25), standardized effect d = -0.12; z-test p = 0.577.
  • Be SMART + MD Review: mean 4.30 versus 4.30 on control; difference 0.00 (95% CI -0.34 to 0.34), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Be SMART Alone and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Be SMART + MD Review and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint, asking whether doctors who take care of children should talk with parents about safe gun storage, measured one month after intervention. Across the groups, responses are high and the arm means are very similar. The recalculated comparisons do not indicate a clear separation of either firearm-safety group from control. The pattern is consistent with the primary results in that neither set of posted comparisons provides precise evidence of a group difference.

The secondary question is related to the study’s broader aim of discussing firearm safety with parents, but it is not the same as the primary behavior measure. The primary endpoint asks how often a parent or guardian asked about guns in another person’s home; the secondary endpoint asks for a view about whether doctors should discuss safe storage. A favorable attitude toward physician discussion does not establish that parents asked more often, that clinicians actually counseled families, or that firearm storage changed. The outcomes capture different aspects of knowledge, attitudes, and practices.

The secondary comparisons are recalculated and unadjusted, and the registry reports no sponsor analyses. A secondary outcome generally carries less confirmatory weight than a prespecified primary outcome, particularly when the analysis plan and multiplicity approach are not available. If several outcomes or comparisons are examined, the chance of at least one apparently notable result can increase unless the analysis accounts for that multiplicity. No adjustment method is reported in the registry record.

The secondary endpoint can therefore add context about respondents’ attitudes, but it does not resolve the uncertainty in the primary comparison or establish an additional physician-review effect. Its interpretation should remain exploratory. Details about whether this outcome was prespecified in the original analysis plan, how missing responses were handled, and whether any other secondary measures were assessed are not reported in the registry record.

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

• Doctors Who Take Care of Kids Should Talk to Parents About Safe Gun Storage at 1 Month Post-intervention

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous score, reported as a mean and standard deviation. A mean describes the average response or average change in a group, while the standard deviation describes how spread out individual values are around that mean. A mean change can be close to zero even when individual participants have moved in different directions; the standard deviation helps show that individual variation is present. Here, the standard deviations are larger than the mean changes, indicating substantial variation in the observed changes within groups.

Why are responses paired?

The primary outcome is defined using responses from the same participant before and after intervention. Those measurements are paired because they are linked within a person. Pairing is generally useful for change questions: each participant serves as a reference for their own baseline, and the analysis can account for the relationship between that person’s two responses. The registry says the primary analysis was limited to paired samples within each group. It does not provide individual-level data or the within-person correlation, so the paired analysis cannot be independently reconstructed from the posted group summaries alone.

The posted comparison values are separately described as recalculated unadjusted comparisons using summary statistics. They compare the mean change in an intervention group with the mean change in control. This is a between-group comparison of change scores, not the same calculation as testing whether each group’s own average change differs from zero. A between-group contrast is generally the more relevant quantity for asking whether assigned groups changed differently, because a pre/post change in one group alone cannot separate intervention effects from changes that might also occur without that intervention.

What do the confidence intervals and p-values describe?

A confidence interval gives a range of values reasonably compatible with the observed estimate under the statistical model used. For the primary comparisons, the recalculated 95% intervals include zero and extend in both directions. Zero represents no difference in mean change between the intervention group and control. Since the intervals also include values on either side of zero, they reflect uncertainty about both the direction and size of any difference. They are not proof that the true difference is zero.

The p-values are unadjusted tests of the respective comparisons under a null hypothesis of no difference. A p-value describes how unusual data at least as incompatible with that null hypothesis would be under the test’s assumptions; it is not the probability that the null hypothesis is true, and it does not measure the probability that an intervention works. The posted p-values do not provide strong evidence against no difference, but that finding should be read with the intervals and sample sizes rather than as proof of equivalence.

What does the standardized effect add?

The registry also gives pooled standard deviations and standardized effect estimates for the recalculated primary comparisons. A standardized mean difference expresses the estimated mean contrast in standard-deviation units, which can help describe magnitude on a scale that is less tied to the original measurement units. The values are -0.064 for Be SMART alone versus control and -0.223 for Be SMART plus physician review versus control. These are estimates from the posted summaries, not separate outcomes or adjusted estimates. Standardization does not resolve uncertainty, establish clinical importance, or make a self-reported scale more directly meaningful.

More generally, statistical precision depends on the amount of information in the data, the variability of responses, and the analysis design. A wide spread of individual changes makes it harder to estimate a group contrast precisely. Pairing can improve precision when repeated measurements within a person are strongly related, but the degree of that relationship is not reported. The posted recalculations use summary statistics, and the registry does not report a detailed model, any covariate adjustment, or the assumptions used in an original sponsor analysis.

Why be cautious about the recalculations?

These comparisons are explicitly recalculated from posted summary statistics and are unadjusted. They should be read as a transparent descriptive comparison rather than as confirmation of the trial’s full planned analysis. The registry reports no analyses in its analysis count, and the sponsor’s own analysis is not reported in the registry record. The original statistical plan, including whether it specified a particular contrast, model, handling of missing data, or multiplicity procedure, is not reported in the registry record.

Randomization supports a causal comparison when assignment and follow-up are handled appropriately, but it does not remove all uncertainty or guarantee that every analysis population remains comparable. The primary outcome’s paired-sample restriction means that the posted primary summaries include participants with both measurements. The record does not say how participants without paired measurements were handled or whether their absence was related to outcomes. This limits assessment of the analysis population and the robustness of the results.

11. Confidence Intervals and Precision

Precision is best judged from the confidence intervals, not from whether an estimate is positive or negative by itself. For Be SMART alone versus control, the recalculated mean difference is -0.1 and its 95% confidence interval is -1.006 to 0.806. For Be SMART plus physician review versus control, the estimate is -0.3 and its 95% confidence interval is -1.085 to 0.485. Each interval includes zero, so each is compatible with no difference as well as with differences favoring either direction.

The intervals are wide in relation to the estimated mean differences. That means the posted results do not pin down the size or direction of a possible between-group difference with much precision. The p-values, 0.829 and 0.454, are consistent with this uncertainty; they are not a substitute for inspecting the full interval. These are recalculated, unadjusted intervals, not sponsor-reported estimates.

Confidence intervals quantify sampling uncertainty under the assumptions of the calculation. They do not account automatically for possible bias from missing paired responses, measurement limitations, deviations from random assignment, or unreported analysis choices. Nor do they say which differences would matter to families or clinicians: a threshold for a meaningful change is not reported in the registry record.

The precision is also limited by the number of paired responses contributing to the primary summaries: 25, 27, and 20 in the three groups. These counts should be read in the context of the recorded enrollment of 225, without assuming why responses were unavailable for the paired analysis. The registry does not report that explanation. Thus, the estimates are informative as descriptions of the posted paired data, but they provide limited certainty about the size of a broader group difference.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations calculated from the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the planning number per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number per arm for a design with a 90% chance under the same assumed effect and model. These are prospective planning concepts: they describe how a future study might be sized, not how likely the current study was to find a result.

For the primary comparison of Be SMART alone with control, the planning figures are 3,892 participants per arm for 80% power and 5,210 for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 6,919 and 9,262 participants per arm; planning for 50% gives 15,567 and 20,839. For the comparison of Be SMART plus physician review with control, the corresponding figures for 100% of the observed effect are 315 and 422 participants per arm; planning for 75% gives 560 and 749, and planning for 50% gives 1,259 and 1,685.

Smaller effects require more participants to detect under otherwise unchanged assumptions. These estimates depend strongly on the observed effect, which is uncertain in a small study, and should not be treated as a reliable forecast without a design-specific effect considered important to detect. This is not observed power; observed power is not a useful way to reinterpret the completed study’s non-significant comparisons.

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 = -0.100; pooled standard deviation σ = 1.575.
2. n = 2 × (1.96 + 0.842)² × 1.575² / -0.100² = 3,891.6, rounded up to 3,892 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 <- -0.1                      # observed difference in means
sigma <- 1.5745061979687                     # 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(3077646)
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 = 3,892 (80% power), 5,210 (90% power)
 75% of observed effect: n per arm = 6,919 (80% power), 9,262 (90% power)
 50% of observed effect: n per arm = 15,567 (80% power), 20,839 (90% power)
power.t.test: 3892.5 
Simulated power at n = 3,892 per arm: 0.797 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The record identifies one primary outcome and one posted secondary outcome, but it does not report a detailed statistical analysis plan or a multiplicity strategy. It is therefore unclear whether the study specified in advance how to handle more than one intervention-versus-control comparison, the secondary endpoint, or any other analyses. The registry reports zero analyses in its analysis count, and no sponsor-reported analysis is posted. The recalculated p-values are unadjusted and should not be interpreted as multiplicity-controlled confirmatory tests.

Multiplicity matters because repeated statistical tests can increase the chance of obtaining at least one small p-value by chance alone. This does not mean that a particular result is false; it means that the evidential weight depends partly on which outcomes and comparisons were planned and how they were analyzed. Those details are not reported in the registry record, so the posted recalculations are best treated as descriptive and exploratory rather than as a complete account of the trial’s intended inferential framework.

The primary outcome analysis is restricted to paired responses from the same participant before and after intervention. The numbers of paired responses differ by group, but the registry does not report why participants lacked a complete pair, how missing responses were handled, whether any imputation was used, or whether a sensitivity analysis was conducted. It also does not report whether the analysis followed the randomized assignment for all participants or instead used another analysis population. The stated paired-sample restriction is the only described population rule for the primary outcome.

The secondary endpoint has larger posted group counts than the primary paired analysis, but the registry does not explain the difference in response availability between outcomes. Missingness could affect the estimate if the participants with observed responses differ systematically from those without them. The available record does not permit assessment of that possibility. Likewise, it does not report baseline balance, protocol deviations, or analysis adjustments that might clarify the comparability of the analyzed groups.

These omissions do not invalidate the posted summaries, but they limit evaluation of bias, reproducibility, and the strength of confirmatory claims. The reason for missing paired data, missing-data methods, analysis populations, multiplicity handling, and sponsor analysis are not reported in the registry record.

15. 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 posted adverse-event summaries list zero serious adverse events and zero other adverse events in each group, with zero deaths reported in each group. The at-risk counts listed are 76 for Be SMART alone, 75 for Be SMART plus physician review, and 74 for control. The registry lists no serious adverse-event terms.

These figures mean that the registry’s adverse-event fields record no events in the listed categories for the stated at-risk groups. They do not establish that no event of any kind occurred outside the reporting definitions or observation period, and they do not demonstrate that the groups have identical safety profiles. When event counts are zero, the data still have limited ability to rule out uncommon events, especially without detailed follow-up and ascertainment information.

The adverse-event at-risk counts are not the same as the paired primary outcome counts. The record does not explain the relationship between these populations or provide detailed adverse-event definitions, collection procedures, or a narrative safety analysis. Those details are not reported in the registry record, so the zero counts should be read narrowly as the posted safety figures rather than as a broader safety conclusion.

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

The results describe a randomized comparison of two firearm-safety information approaches with a tobacco-smoke-exposure control in parents or guardians in a pediatric inpatient study. For the primary self-reported asking-frequency outcome, all groups had positive average change scores, while the recalculated intervention-versus-control differences were small relative to their uncertainty. The confidence intervals include zero and are broad enough to accommodate differences in either direction.

That pattern does not establish that the firearm-safety interventions changed the behavior more than control, and it does not establish that they had no effect. The estimates are too imprecise to distinguish confidently among no difference and a range of possible differences. The results also do not establish whether physician review adds an effect beyond the video and written materials. The secondary attitude measure provides related context but cannot substitute for evidence about the primary behavior.

The endpoint is self-reported asking frequency during a specified recall period. It does not measure whether a home contained firearms, whether firearms were stored safely, whether a conversation changed anyone’s decisions, or whether children experienced fewer firearm-related harms. Those outcomes are not posted as results in the registry record. A change in an attitude or reported behavior should not be treated as proof of a change in storage conditions or clinical outcomes.

Interpretation is further limited by the paired-sample analysis population, the absence of a reported explanation for missing paired responses, and the lack of a posted sponsor analysis or detailed statistical plan. The recalculated estimates are unadjusted and should be read as analyses of the posted summaries, not as a substitute for a full trial report. The results apply most directly to the participants whose responses contribute to those summaries and to the particular measures recorded.

In short, the registry data show similar average change patterns across groups but do not provide precise evidence that either firearm-safety approach outperformed the control on the primary measure. They leave the magnitude and direction of a possible difference uncertain and do not answer broader questions about firearm storage or child safety outcomes.

17. Why This Trial Matters Statistically

This study addresses a statistical question about a setting and an intervention format: whether an inpatient encounter, brief video, written materials, and optional physician review are associated with different changes in a reported safety-related behavior. Separating the intervention components is useful because the design includes a video-and-handout group as well as a group receiving physician review. The control also helps distinguish changes occurring in the intervention groups from changes that may occur over the same period without firearm-safety content.

The primary outcome illustrates why a randomized comparison should focus on differences between groups rather than treating improvement within one group as evidence of an intervention effect. The control group also had a positive mean change. Comparing each intervention group with control is therefore central to interpreting whether changes differed by assignment. The posted recalculations show that those contrasts are uncertain, rather than establishing a clear advantage or equivalence.

The study also illustrates how endpoint choice shapes the claim that can be made. Asking about guns in another person’s home is a specific self-reported practice. A secondary question about doctors’ role in discussing safe storage concerns attitudes. Neither measure directly captures safe storage behavior or downstream health outcomes. Clear distinctions among behavior, attitude, and clinical outcomes prevent results from being interpreted more broadly than the measurements allow.

Finally, the record underscores the importance of reporting paired analysis populations, missing-data handling, prespecified comparisons, and the sponsor’s analysis. Without those details, readers can describe the posted estimates and their uncertainty, but cannot fully assess whether the calculations match the intended plan or how missing responses may affect inference. These are central considerations in clinical trial interpretation, especially when the available estimates are imprecise.

18. Limitations

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

The primary results are based on paired responses from a subset of the recorded enrollment. The registry does not explain why some participants did not contribute paired measurements, how missing data were handled, or whether the missingness differed by group. That leaves uncertainty about how representative the analyzed responses are of all randomized participants.

The outcome is self-reported and concerns asking about guns in another person’s home over the last 30 days. The record does not report validation of the scale, whether responses were checked against observed behavior, or a threshold for a meaningful change. The measure may not capture other relevant firearm-safety practices. The registry does not report outcomes on firearm storage, access, or child injury.

The comparisons are recalculated, unadjusted analyses from posted summary statistics. No sponsor analysis or detailed statistical plan is reported, and multiplicity handling is not reported. The record also does not provide the random-sequence method, allocation concealment details, or further information about masking beyond listing the study as unmasked. These gaps limit evaluation of the analysis and possible sources of bias.

Interpretation of the secondary endpoint is also constrained by its different construct and its unadjusted status. The record does not report whether the outcome was prespecified in a formal analysis plan, how missing secondary responses were handled, or whether other secondary measures were analyzed. Finally, the planning illustrations use observed effects and should not be read as the trial’s original design justification. These are limitations of the available registry record; further detail is not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pediatric Inpatient Firearm Safety Study — NCT03077646.
• Registry record last updated 2021-02-23; status last verified 2021-02.
• Results first posted 2021-02-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03077646, the Pediatric Inpatient Firearm Safety Study, is recorded as a completed randomized, unmasked, parallel-group study sponsored by Montefiore Medical Center. Recorded enrollment is 225. The three groups received Be SMART video and written materials, the same intervention with physician review, or tobacco-smoke-exposure control materials.

The primary outcome is paired change in the frequency of asking whether another person’s home has guns when a child visits. The posted primary group means show similar positive changes, while recalculated unadjusted comparisons with control have confidence intervals that include zero. The results are imprecise and do not establish a clear between-group difference. One secondary attitude outcome is posted; its group pattern is also similar.

The registry records zero serious adverse events, zero other adverse events, and zero deaths in the listed groups. A detailed statistical analysis plan, sponsor analysis, missing-data explanation, and multiplicity approach are not reported in the registry record.