Hostile Bias Modification Training Online Study II: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hostile Bias Modification Training Online Study II (NCT04015440), a randomized na study. The primary outcome is Hostile Attribution Bias.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, parallel-group behavioral study. The registry reports enrollment of 229 participants and a completed study. The study start date was 2019-07-30, and primary completion was 2019-12-31. The record describes two parts: participants first completed surveys, hypothetical scenarios, and a vocabulary task, then returned 24–96 hours later for a similar scenario activity and a brief questionnaire about recent behavior.

Participants were assigned to HBMT or placebo. The posted primary outcome summaries include 109 participants in the HBMT arm and 108 in the placebo arm. The record does not explain the difference between total enrollment and the arm counts reported for this outcome, or whether those counts reflect an analysis population, missing outcome data, or another reason. The identity of the masked party is not reported in the registry record.

The study lists aggression, anger, emotion regulation, self-control, and stress as conditions. It lists anger as a secondary outcome, and the registry record posts results for one secondary outcome. The phase is listed as not applicable. Details of the randomization method, allocation concealment, exact placebo procedure, and planned statistical analysis are not reported in the registry record. In particular, the original sample-size justification and any planned interim analyses are not reported.

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.

Population: Adults (18 years old or older) in the United States responding to online advertisement on Amazon Mechanical Turk.

6. Primary Endpoint

The registry lists the primary outcome as Hostile Attribution Bias, measured over 24-96 hours post HBMT.

The primary endpoint is hostile attribution bias, expressed as a score on a scale and summarized as a mean with a standard deviation. Volunteers read hypothetical scenarios in which another person acted aggressively but the intention was uncertain. They rated how likely they would be to think hostile thoughts about the situation. The score was formed from responses to items within scenarios and averaged across scenarios.

One set of four scenarios was used at the first time point and a second set of five at the second time point. Individual scores at either time point could range from 0, indicating no hostile attribution bias, to 24, indicating high hostile attribution bias. The reported primary endpoint was assessed 24–96 hours after HBMT.

This measure addresses the study’s stated question about how responses to a word-completion task relate to interpretation and behavior in everyday situations. Using a defined score permits a quantitative comparison between the randomized arms. It captures participants’ interpretations of hypothetical situations, however; it is not itself a direct measure of real-world aggressive behavior. The registry record does not report additional measurement properties or explain how the second-time-point scenarios were selected beyond describing them as a second set.

7. Results Posted in the Registry

• HBMT: mean 9.40 versus 10.80 on control; difference -1.40 (95% CI -2.44 to -0.36), standardized effect d = -0.36; z-test p = 0.008.

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.

Anger

• 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:
  • HBMT: mean 1.90 versus 1.70 on control; difference 0.20 (95% CI -0.07 to 0.47), standardized effect d = 0.20; z-test p = 0.143.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HBMT and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome, anger. The direction and precision of that unadjusted comparison do not provide a clear statistical counterpart to the primary hostile attribution bias finding: the secondary interval includes no difference. This means the secondary outcome does not offer clear evidence of an arm difference in the posted recalculation, but it also does not establish that the arms are equivalent or that a difference is absent.

The two outcomes measure different constructs. Hostile attribution bias concerns interpretation of ambiguous scenarios, while the secondary measure is anger. A result for one should not be assumed to imply a result for the other. The primary result therefore remains specific to its own score, time point, and analysis rather than serving as proof of a broader pattern across outcomes.

Unadjusted secondary results generally carry less weight when multiple outcomes or comparisons are considered, because the chance of at least one apparently unusual result can increase as more tests are examined. A multiplicity adjustment or prespecified hierarchy can address this issue, but such a strategy is not reported in the registry record. The registry lists four outcome measures, reports one secondary outcome, and lists three analyses; the record does not explain how those counts relate or whether all planned outcomes and analyses are posted. Without that information, the secondary result should be treated as limited supporting context rather than a definitive confirmation or contradiction of the primary result.

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

• Anger

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

The recalculated mean difference is the HBMT group mean minus the placebo group mean. For the primary outcome, that estimate is -1.4 points. A negative value indicates that the HBMT group had the lower observed mean on the hostile attribution bias scale. The estimate is unadjusted: it uses the posted group summaries rather than a regression model that adjusts for other variables.

What does a confidence interval tell the reader?

In general, a confidence interval describes the range of estimates compatible with the observed data under the assumptions of the method. It conveys uncertainty around a point estimate; it is not a range containing a known fraction of individual participants’ scores. For the primary recalculation, the reported 95% interval excludes zero, the value corresponding to no mean difference. This gives evidence against a zero unadjusted mean difference under the calculation’s assumptions, while still allowing uncertainty about the size of the difference.

What do the standard deviations add?

The reported standard deviations describe variation among scores within each arm. Both primary-outcome standard deviations are 3.9. The standard deviation is not the standard error of the mean and does not directly describe uncertainty in the estimated arm difference. The posted recalculation uses the group sizes and variability to estimate that uncertainty. A standardized effect-size estimate, Cohen’s d, is also posted as -0.359. It expresses the estimated difference relative to pooled variability, but the registry record does not provide a threshold for interpreting what size of standardized difference is important.

How should the p-values be read?

In general, a p-value describes how incompatible the observed data, or results more extreme, are with a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The recalculated unadjusted primary p-value is 0.008. The sponsor’s linear-regression analysis reports p <.001. Because the registry does not give the regression estimate, confidence interval, or model details, these p-values should be understood as results from separately described analyses, not as interchangeable summaries.

Why distinguish adjusted and unadjusted analyses?

An unadjusted comparison uses the observed group summaries without accounting for additional measured factors. Regression can estimate a group contrast while accounting for covariates or other model terms, but the registry does not report which terms, if any, were included. Adjusted and unadjusted estimates can differ because they may answer differently specified statistical questions. The record does not provide enough detail to identify why the sponsor’s reported p-value differs from the recalculated one.

Why can over-dispersion matter?

In general, over-dispersion means that the observed variability is greater than a statistical model assumes. If a model underestimates variability, standard errors can be too small and confidence intervals too narrow; inference can then appear more precise than warranted. The posted primary outcome is analyzed as a continuous score with means and standard deviations. The registry record does not report a dispersion assessment or model diagnostics, so there is no basis to state whether over-dispersion was assessed or affected the sponsor analysis.

What does the planning illustration mean?

The sample-size illustrations use the observed effect as a planning reference and consider smaller fractions of that effect. They give participants per arm for two-sided testing at a significance level of 0.05, equal allocation, and a normal approximation. These are planning calculations, not observed trial results. A target of 80% power or 90% power describes the probability, under the assumptions of the calculation and a specified effect, of rejecting a null hypothesis when that effect is present. The registry does not report the study’s own original design assumptions or sample-size justification.

11. Confidence Intervals and Precision

The primary recalculation estimates an unadjusted mean difference of -1.4 points, with a 95% confidence interval that excludes zero. The interval therefore indicates that the observed data are not equally compatible with every possible difference: values near no difference are less consistent with this calculation than values on the negative side. The interval still represents uncertainty about the magnitude of the underlying contrast. A confidence interval is not a guarantee that the true effect lies within its limits.

The group standard deviations are 3.9 in both arms, and the posted group sizes are 109 for HBMT and 108 for placebo. These summaries help describe the information contributing to the unadjusted estimate. They do not remove uncertainty or establish whether a difference is important to participants. The record does not report a threshold for practical or clinical importance, so statistical evidence and importance should not be treated as the same question.

The sponsor’s regression analysis reports p <.001, but its estimate and confidence interval are not reported in the registry record. Consequently, the precision of that model-based estimate cannot be assessed from the posted regression result alone. The recalculated interval applies to the unadjusted comparison of group means and should not be presented as the interval for the sponsor’s regression.

For the secondary anger outcome, the recalculated interval spans zero, indicating that the unadjusted estimate is compatible with differences in either direction under the calculation. That interval does not demonstrate equivalence or prove there was no difference. More broadly, the short 24–96-hour assessment window and unreported information about missing data, outcome availability, and analysis populations limit what can be inferred about precision beyond the posted summaries.

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 event counts. This is a continuous-outcome comparison, so the figures concern the number of participants in each of two equally allocated arms. The calculations use a two-sided significance level of 0.05 and a normal approximation. They illustrate planning for the observed effect and for smaller fractions of that effect. For example, the listed scenarios include planning for 75% of the observed effect and 50% of the observed effect; the participant requirements rise as the assumed effect becomes smaller.

The 80% power column gives the estimated participants per arm under the stated assumptions for an 80% chance of detecting the specified effect if that effect is present. The 90% power column gives the corresponding per-arm requirement for a 90% chance. Greater power generally requires more participants, and detecting a smaller effect also requires more participants when other assumptions are held fixed. The listed values are planning illustrations based on the observed effect, not evidence that the completed study had a particular probability of detecting an effect.

These figures are not observed power. They do not describe a measured property of the completed trial, and they are not the trial’s original design calculation. The registry record does not report the original sample-size justification or the assumptions used when the study was designed. The calculations therefore help readers understand how assumed effect size and target power affect planning, but they cannot establish whether the study met its original recruitment target or was designed around the effect ultimately observed.

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 = -1.400; pooled standard deviation σ = 3.900.
2. n = 2 × (1.96 + 0.842)² × 3.900² / -1.400² = 121.8, rounded up to 122 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 <- -1.4                      # observed difference in means
sigma <- 3.9                     # 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(4015440)
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 = 122 (80% power), 164 (90% power)
 75% of observed effect: n per arm = 217 (80% power), 290 (90% power)
 50% of observed effect: n per arm = 488 (80% power), 653 (90% power)
power.t.test: 122.8 
Simulated power at n = 122 per arm: 0.798 (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 reports a sponsor analysis using linear regression for the primary comparison, with p <.001. It does not report the regression coefficient, its confidence interval, the variables included in the model, or other model details. The sponsor’s result is therefore available as a p-value but not as a fully described estimate of the difference and its precision.

A separate recalculation from the posted arm means and standard deviations gives an unadjusted mean difference of -1.4 points, a 95% confidence interval excluding zero, and an unadjusted p-value of 0.008. This recalculation does not reproduce the regression model. The registry record does not explain why the reported regression p-value differs from the unadjusted result, and the available information is insufficient to attribute the difference to adjustment, model specification, or another cause.

The two results should be read as distinct analyses with different reported detail. The sponsor’s analysis is the analysis reported in the registry; the recalculation provides a transparent, unadjusted comparison using the group summaries. The registry record does not report a discrepancy flag, but that does not supply the missing regression estimate or explain the relationship between the analyses. Neither p-value alone describes the size or practical importance of the contrast.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or statistical tests are examined. In general, repeated testing can increase the chance of obtaining at least one small p-value even when no real differences exist. Researchers may address this through a prespecified primary outcome, adjustment procedures, or a planned testing sequence. The registry identifies hostile attribution bias as the primary outcome and anger as a secondary outcome, but a multiplicity strategy is not reported in the registry record.

The record lists four outcome measures and three analyses, while posting results for the primary outcome and one secondary outcome. It does not explain whether the remaining measures were not assessed, were assessed but not posted, or were handled in another way. It also does not report whether the posted secondary result was adjusted for multiple testing. Accordingly, unadjusted secondary evidence warrants cautious interpretation, and the extent of selective reporting cannot be determined from the record alone.

Information about missing data and analysis populations is also limited. The registry reports total enrollment of 229 and gives primary-outcome group counts of 109 and 108, but does not explain how the reported counts relate to the full enrollment. Reasons for missing outcome data, if any, are not reported. The record does not describe an intention-to-treat population, a per-protocol population, exclusion criteria for analysis, or methods used to handle missing scores.

The randomization method, allocation concealment, covariate adjustment, model diagnostics, and prespecified handling of deviations are not reported in the registry record. These omissions do not show that such procedures were absent; they mean that readers cannot evaluate them from the posted record. The stated statistical significance should therefore be considered alongside uncertainty about the analysis plan, outcome availability, and multiplicity.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The registry reports zero serious adverse events in the HBMT arm among 109 participants at risk and zero in the placebo arm among 108 participants at risk. It also reports zero other adverse events in each arm, using the same at-risk counts. No deaths are reported in either arm. No serious adverse event terms are listed.

These are the adverse-event counts recorded in the registry. Zero recorded events does not establish that an event is impossible, that all events were captured, or that the two arms have identical safety profiles. The registry record does not provide definitions, collection procedures, follow-up duration for adverse-event reporting, or a narrative assessment of the safety data. The figures should be read as event counts within the reported at-risk groups, not as a guarantee about risk beyond the recorded study period.

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

The posted primary data show a lower mean hostile attribution bias score in the HBMT arm than in the placebo arm at 24–96 hours after training. The unadjusted recalculated difference is -1.4 points, and its 95% confidence interval excludes zero. The sponsor’s regression analysis also reports a small p-value, although its estimate and interval are not given in the registry record. These results describe a group-level contrast on the stated measure and at the stated follow-up.

They do not establish that participants behaved differently in real-world situations. The primary score comes from responses to hypothetical scenarios, and the registry summary does not report a direct behavioral endpoint corresponding to actual aggression. The result also does not establish how long any observed difference might last: the primary assessment was 24–96 hours after training, and longer-term outcomes are not reported in the registry record.

The findings do not by themselves determine whether the size of the score difference is important. The record does not report a threshold for a meaningful change. Nor should a result on hostile attribution bias be generalized to anger, emotion regulation, self-control, or stress. The posted secondary evidence is limited, and multiplicity, missing-data handling, and analysis-population details are not reported.

Statistical evidence about a difference is distinct from evidence about mechanism, durability, or practical consequences. The registry record supports a description of the observed scores and the stated analyses; it does not establish broader clinical or behavioral effects. Interpretation should therefore stay within the randomized comparison, the measured construct, the short follow-up window, and the information actually reported.

18. Why This Trial Matters Statistically

This study illustrates why an endpoint’s meaning matters as much as its numerical result. Hostile attribution bias is measured through interpretations of ambiguous hypothetical situations. The score makes those responses suitable for a group comparison, but it is not the same as directly observing behavior. Statistical interpretation should connect the estimate to the construct actually measured rather than extending it to broader outcomes.

The record also shows the value of distinguishing a sponsor-reported model from an unadjusted recalculation. The regression result is reported as a p-value without an estimate or confidence interval, while the recalculation supplies a mean difference and uncertainty based on the arm summaries. Keeping those analyses separate avoids treating results with different levels of detail as interchangeable.

Finally, the registry record makes visible important limits on evaluation: the original design assumptions, multiplicity strategy, analysis populations, missing-data methods, and regression details are not reported. Those details affect how readers assess precision and robustness. Planning illustrations can clarify how target power and assumed effect size relate to participant requirements, but they cannot substitute for the study’s original design rationale. This is a useful example of interpreting a short-term behavioral outcome while keeping the statistical claim proportional to the posted evidence.

19. Limitations

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

The primary outcome is based on participants’ responses to hypothetical scenarios. Although the study summary connects the task with real-world interpretation and behavior, the posted primary endpoint does not directly record real-world behavior. The follow-up interval is 24–96 hours after training, so the registry results do not address durability beyond that window.

The registry record does not describe the content of the placebo training or provide detailed procedural information about HBMT. It identifies the study as single-masked but does not say who was masked. Randomization procedures and allocation concealment are also not reported. These omissions limit assessment of how the study was implemented, without showing that particular safeguards were absent.

The sponsor’s regression analysis lacks a reported estimate, confidence interval, and model specification. The unadjusted recalculation is informative about the posted arm summaries but cannot replace an assessment of that model. Details about missing outcome data, analysis populations, and the difference between total enrollment and reported outcome group counts are not reported. The registry also does not report a multiplicity plan, a meaningful-change threshold, or the original sample-size justification.

Results are posted for the primary outcome and one secondary outcome, while the record lists more outcome measures and analyses. The completeness of outcome reporting cannot be established from the registry record. These limitations constrain interpretation of precision, robustness, and generalizability beyond the measures and time point described.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Hostile Bias Modification Training Online Study II — NCT04015440.
• Registry record last updated 2021-09-08; status last verified 2021-08.
• Results first posted 2021-09-08.
• 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

NCT04015440 is a completed randomized, single-masked, parallel-group behavioral study of online Hostile Bias Modification Training compared with placebo. The registry reports enrollment of 229 participants. Its primary outcome is hostile attribution bias, measured as a score on a scale 24–96 hours after training.

The posted primary arm means are 9.4 for HBMT and 10.8 for placebo. The unadjusted recalculated mean difference is -1.4 points, with a 95% confidence interval excluding zero and an unadjusted p-value of 0.008. The sponsor reports a linear-regression p-value of <.001 but does not report the estimate or its confidence interval. One secondary outcome, anger, is posted. The record does not report the original sample-size rationale, multiplicity plan, missing-data methods, or analysis-population details.