LA-CEAL 4.0: Wearable Sensor Project: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for LA-CEAL 4.0: Wearable Sensor Project (NCT06086028), a randomized na study. The primary outcome is Percentage of Days in Concordance Comparing Immediate Information Period With Delayed Information Period.

2. Clinical Question

3. Trial Design

LA-CEAL 4.0: Wearable Sensor Project is recorded as a randomized, unmasked crossover study sponsored by Tulane University. The registry lists the study as completed, with planned enrollment of 80. The conditions listed are health care workforce burnout and stress. The study is not assigned a conventional drug-development phase; the phase entry is NA.

The intervention was a wrist-worn sensor. Participants were assigned to an order of information availability. In the Immediate then Delayed Arm, participants had immediate access to sensor data for the first 21-day feedback period; on day 22, the data were hidden until after the second 21-day period. In the Delayed then Immediate Arm, data were initially hidden and became available in real time for the second period. Thus, the comparison concerns the timing of access to information from the sensor, rather than a comparison between sensor use and no sensor use.

A crossover design lets a participant contribute observations under both conditions. That can be useful when the outcome is measured repeatedly, but the interpretation depends on how the analysis accounts for within-participant correlation, period effects, and the order in which conditions occurred. The registry record does not report the randomization method, whether the analysis adjusted for period or sequence, or whether any carryover effects were assessed. Masking is listed as none, so the study was unmasked.

The primary outcome covers six weeks. The record says 71 participants were monitored during both immediate and delayed information periods. It does not describe the analysis population in further detail or explain how incomplete observations were handled. The registry lists a start date of 2023-11-20 and primary completion date of 2024-05-31.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Cross-over design. 71 participants were monitored during both immediate and delayed information periods.

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 Percentage of Days in Concordance Comparing Immediate Information Period With Delayed Information Period, measured over 6 weeks.

The primary endpoint is the percentage of days in concordance when comparing immediate information with delayed information. Concordance was derived from responses to two questions: how stressed a participant felt that day, and whether they completed a self-care activity that day. A stress response of 6+ on the 1–10 scale was coded as high stress. A day was counted as concordant when a participant reported high stress and engaged in self-care, or reported low stress and did not engage in self-care. The outcome was calculated separately for each 21-day feedback period.

This measure is intended to capture alignment between reported stress, self-care behavior, and the participant’s access to biometric information. It is not a direct measure of stress alone, nor does it directly establish that the sensor changed stress or burnout. Its value depends on the accuracy and completeness of daily responses and on the interpretation of the concordance rule. The registry describes the endpoint as a mean, with standard deviation as the measure of spread.

The reported mean values are 0.49 for the immediate-information period and 0.5 for the delayed-information period. The registry reports the delayed-minus-immediate mean difference as 0.01. A near-zero point estimate alone does not show how precisely the difference is known; uncertainty is conveyed by the confidence interval and should be considered alongside the estimate.

7. Results Posted in the Registry

• Delayed Information Period: mean 0.50 versus 0.49 on control; difference 0.01 (95% CI -0.06 to 0.08), standardized effect d = 0.05; z-test p = 0.773.

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.

Change in Burnout Score From Baseline to Follow-up (Pre/Post Sensor Data Collection)

• 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:
  • 6 Weeks Follow up: mean 35.54 versus 38.82 on control; difference -3.28 (95% CI -10.40 to 3.84), standardized effect d = -0.17; z-test p = 0.366.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 6 Weeks Follow up and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one posted secondary result: change in burnout score from baseline to six weeks follow-up. It is conceptually related to the study’s focus on stress and burnout, whereas the primary endpoint captures concordance between reported stress, self-care activity, and access to sensor information. These outcomes address related but distinct questions. A result on concordance cannot be treated as a direct estimate of change in burnout, and a burnout score does not directly establish whether participants’ daily responses aligned with the study’s concordance rule.

The overall pattern does not offer a clear, statistically precise signal that complements the primary comparison. The secondary estimate has an interval spanning zero and an unadjusted p-value. It therefore carries uncertainty and should not be used to strengthen a claim beyond what the primary result supports. The posted analyses do not report an adjusted inference for this outcome.

Secondary results generally carry less confirmatory weight when many outcomes or comparisons may be examined. Testing several outcomes can increase the chance that at least one appears notable by chance. Adjustment methods or a prespecified hierarchy can address that concern, but the registry record does not report whether such procedures were planned or used. It lists 11 outcome measures, while only one secondary result is posted, and reports no analyses for the secondary outcome beyond the posted summary. The available record does not clarify which outcomes were intended to be confirmatory or whether unposted outcomes were analyzed.

For these reasons, the secondary result is best treated as contextual information rather than independent confirmation of the primary finding. The key interpretive limitation is not simply whether a secondary p-value crosses a threshold; it is the uncertainty in the estimate, the relationship between the different endpoints, and the absence of information about multiplicity and the full analysis plan.

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

• Change in Burnout Score From Baseline to Follow-up (Pre/Post Sensor Data Collection)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes the primary outcome as a mean of a continuous measure, with standard deviation as its dispersion measure. The comparison is reported as a mean difference. These statistics address different aspects of the result: the mean describes the average observed outcome in a condition, the mean difference describes the contrast between condition means, and the standard deviation describes variability among observations around a mean.

What does a mean difference represent?

A mean difference expresses the contrast between two group or condition averages on the outcome’s original scale. The direction depends on the order of subtraction. For this comparison, the registry reports delayed minus immediate, so a positive estimate indicates a higher mean in the delayed period than in the immediate period. The estimate is 0.01. Its interpretation should remain tied to the concordance measure and its recorded scale; it is not a change in a percentage unless the outcome is explicitly converted to that form.

A mean difference is useful because it retains the units and scale of the original endpoint. However, an average does not show whether observations are concentrated near the mean or widely dispersed. The reported standard deviations help describe that variation, though they do not reveal the full shape of the outcome distribution. The registry’s reported standard deviations for the primary periods are 0.03 and 0.29.

Why does the crossover design affect analysis?

In a crossover study, participants contribute measurements under more than one condition. Their measurements can be correlated because characteristics of a participant persist across periods. An analysis that treats all period observations as independent may not represent that dependence correctly. Appropriate methods can account for repeated observations, but the registry record does not report which method was used for the primary comparison.

Crossover studies can also be affected by the order of conditions and by changes over time. A period effect is a difference associated with being observed in one period rather than another, regardless of the information condition. A carryover effect occurs when experience in an earlier period influences outcomes in a later period. These are general design considerations, not claims that such effects occurred in this study. Whether the sponsor evaluated them is not reported in the registry record. The record describes two treatment sequences and says the participants were monitored in both conditions, but does not report sequence-specific outcomes or an adjusted model.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data under the method’s assumptions. It communicates uncertainty in an estimate, rather than only reporting a single point. For the primary comparison, the interval includes zero and extends to both negative and positive values. That means the posted estimate does not precisely distinguish a difference in one direction from no difference or a difference in the other direction. The confidence level and interval construction method are not reported in the registry record, so the interval should be interpreted as reported rather than assigned an unreported method.

The interval’s width matters as much as whether it includes zero. A broad interval leaves more uncertainty about the magnitude of the effect. In general, precision depends on the amount and variability of information and on the analysis method. In a crossover design, the relationship between measurements from the same participant can also affect precision. The summary does not include enough detail to assess how those elements were handled.

What does the p-value add?

The primary comparison has an unadjusted p-value of 0.773. In general, a p-value measures how compatible the observed result is with a specified null model, assuming the model and its assumptions hold. It does not tell whether an effect is important, whether the null is true, or whether the study had adequate precision. The p-value is described as unadjusted; the registry record does not report a multiplicity adjustment or a fuller statistical analysis plan.

For the crossover comparison, interpreting the p-value also depends on the method used to analyze repeated observations. The record does not identify that method. Therefore, the p-value is best treated as the registry’s reported unadjusted result, not as independent confirmation of the point estimate or as a substitute for the interval.

How should the secondary outcome be understood?

The secondary outcome is a continuous burnout score measured at baseline and six weeks follow-up. The registry reports a mean difference and confidence interval, along with an unadjusted p-value. For continuous outcomes, the same broad principles apply: the mean difference describes the contrast on the score scale, the interval conveys uncertainty, and the p-value is conditional on the analysis assumptions. The record does not report a separate analysis plan for this endpoint or any adjusted secondary analysis.

Secondary outcomes can provide complementary information, but interpretation is more difficult when many outcomes or comparisons are considered without adjustment. The registry lists 11 outcome measures and one posted secondary result. It does not report how many outcomes were prespecified as confirmatory, whether all planned outcomes were posted, or whether the analysis accounted for multiple testing. Those omissions limit the strength of conclusions drawn from a single unadjusted secondary result.

These statistical explanations are general. They clarify the meaning of the reported summaries, but they do not supply missing details about the trial’s analysis procedures. The analysis model, missing-data strategy, and original statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 0.01 for delayed compared with immediate information. The reported confidence interval crosses zero, extending from a negative value to a positive value. This indicates that the posted data do not pin down the direction of the underlying difference with precision. The interval includes no difference as well as possible differences in either direction under the reported analysis.

The result should not be summarized only by its point estimate. An estimate close to zero can coexist with substantial uncertainty, and an interval that includes zero does not prove that the conditions are equivalent. Equivalence would require an appropriate design and a prespecified margin defining what differences would count as sufficiently small; such a margin is not reported in the registry record.

The standard deviations reported for the periods are 0.03 for immediate information and 0.29 for delayed information. This contrast in observed spread cautions against relying on a single average to characterize the outcome. The record does not provide distributions, participant-level data, or an explanation for the difference in spread. Nor does it report the confidence-interval method or an adjustment for the repeated measurements inherent in the crossover design.

The primary comparison’s unadjusted p-value is 0.773. It does not remove uncertainty or establish that the conditions have the same effect. Precision is better assessed from the estimate and its interval, together with study design and analysis details. Since the registry record does not report those details fully, the result supports a cautious reading: the estimated contrast is small on the posted scale, but its magnitude and direction remain uncertain.

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 calculations are planning illustrations based on the observed effect, not the trial’s original design assumptions. The original sample-size justification and design assumptions are not reported in the registry record. For this continuous outcome, the listed figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario targets a stated fraction of the observed effect.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding number for a 90% chance. These are design-planning quantities, not probabilities that the reported trial result is true. They are also not observed power.

The table varies the effect used for planning. It includes planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For example, planning for 100% of the observed effect gives 6,672 participants per arm for 80% power and 8,932 participants per arm for 90% power. Planning for 75% gives 11,861 participants per arm for 80% power and 15,878 participants per arm for 90% power. Planning for 50% gives 26,687 participants per arm for 80% power and 35,726 participants per arm for 90% power.

The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation and therefore require more participants under otherwise unchanged assumptions. These illustrations should not be read as a recommendation for a future study. They do not incorporate any unreported features of the crossover design or its analysis, and they are based on an observed estimate that is itself uncertain. A planning curve, if viewed alongside the figures, expresses the same relationship between assumed effect size and planned sample size.

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 = 0.010; pooled standard deviation σ = 0.206.
2. n = 2 × (1.96 + 0.842)² × 0.206² / 0.010² = 6,671.5, rounded up to 6,672 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 <- 0.01                      # observed difference in means
sigma <- 0.206155281280883                     # 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(6086028)
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 = 6,672 (80% power), 8,932 (90% power)
 75% of observed effect: n per arm = 11,861 (80% power), 15,878 (90% power)
 50% of observed effect: n per arm = 26,687 (80% power), 35,726 (90% power)
power.t.test: 6672.5 
Simulated power at n = 6,672 per arm: 0.803 (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 registry record does not report a multiplicity strategy. This matters because the record lists 11 outcome measures and includes a primary endpoint as well as a posted secondary result. When multiple outcomes or comparisons are analyzed, the chance of at least one apparently unusual result can increase. A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory analyses can help readers understand the strength of evidence. Whether any of these approaches was used is not reported in the registry record.

The primary p-value is identified as unadjusted, and the secondary p-value is also reported as unadjusted. No reported analyses are listed for the secondary outcome. These entries do not establish that no additional analyses were conducted; they mean that the registry record does not report them. The statistical analysis plan, including any treatment of multiple outcomes, is not reported in the registry record.

Missing-data handling is also not reported. The primary description says 71 participants were monitored during both periods, while planned enrollment was 80. The record does not explain why those counts differ, how many observations were available for each endpoint, whether any daily responses were missing, or how incomplete period data were handled. The secondary outcome reports 57 observations at baseline and 57 at follow-up, but does not say how missing values were treated or whether the paired nature of the measurements was incorporated in the comparison.

The analysis population is not fully defined. The record does not state whether the primary result used all randomized participants, only participants with observations in both periods, or another population. It also does not describe exclusions, protocol deviations, or the handling of participants who did not complete the assigned sequence. These details affect how broadly the results can be interpreted and how well the analysis preserves the randomized comparison.

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

The posted primary result describes a mean concordance value of 0.49 during immediate information access and 0.5 during delayed access, with a reported mean difference of 0.01. The comparison is uncertain: its confidence interval crosses zero, and the unadjusted p-value is 0.773. The data therefore do not provide a precise estimate of the direction or size of a difference in this outcome.

This result does not show that immediate sensor information improves or worsens stress management. The primary endpoint combines self-reported stress with reported self-care activity according to a defined concordance rule. It is not a direct measure of clinical burnout, and it does not by itself indicate whether participants’ stress symptoms changed. The study’s secondary burnout score is a separate outcome and is also uncertain in the posted summary.

Nor does an interval crossing zero demonstrate that immediate and delayed information are equivalent. Equivalence requires a prespecified range of differences considered unimportant and an analysis designed to evaluate that range. No equivalence margin is reported in the registry record. Likewise, a non-significant unadjusted p-value is not proof of no effect; it may reflect uncertainty, limitations in the data, or features of the analysis that cannot be evaluated from the registry summary.

The study is a randomized, unmasked crossover study, with participants monitored during immediate and delayed periods. That design provides a basis for comparing information conditions within participants, but interpretation depends on how repeated measurements, period effects, and sequence are handled. Those analysis details are not reported in the registry record. The result should therefore be understood as the posted summary of the comparison, not as a complete account of the analysis.

In practical terms, the registry results offer an estimate of concordance under each information condition but do not establish a reliable difference between them or a change in burnout attributable to access to sensor data. No medical advice follows from these statistics. Further interpretation would require details about the analysis, missing data, and outcomes beyond the summaries posted in the registry record.

16. Why This Trial Matters Statistically

This study is statistically interesting because it evaluates a behavioral feedback question using a crossover design. Participants encountered immediate and delayed access to wearable-sensor information, allowing the outcome to be compared across information conditions within a study structured around both periods. For biostatisticians and clinical researchers, that design raises important questions about repeated measurements, participant-level correlation, period effects, and sequence.

The endpoint is also a composite behavioral classification rather than a direct physiological or clinical measure. It combines answers about perceived stress and self-care activity, using a rule to label days concordant. That makes the outcome relevant to the study’s question about attending to biometric information, while also making its interpretation dependent on how responses were obtained and how missing daily entries were treated. The registry record does not report those data-handling details.

The posted estimate is close to zero, but the confidence interval crosses zero and the periods have markedly different reported standard deviations. This is a useful reminder that an average contrast, its uncertainty, and the distribution of observations each contribute to interpretation. The unadjusted p-value does not resolve these questions. The absence of reported model details and multiplicity procedures further limits what can be concluded from the summary.

The study also illustrates why registry completeness matters. The record describes randomized sequences and a planned enrollment, but does not give the original sample-size justification, a full analysis plan, or a missing-data strategy. Such information helps readers distinguish a design-stage decision from a retrospective planning illustration and assess whether the published summary aligns with the intended analysis. The posted sample-size illustrations are based on the observed effect and should be understood as planning calculations, not evidence of the study’s achieved power.

17. Limitations

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

Several limitations specific to this study constrain interpretation of the registry results. The primary outcome depends on daily self-reports about stress and self-care. The record describes how concordance was classified but does not report response completeness, validation of the questions, or the treatment of days with missing responses. The effect of incomplete daily reporting on the period averages is therefore not assessable from the registry record.

The crossover design requires attention to repeated observations and to whether order or period influences the outcome. Although the registry describes the immediate-then-delayed and delayed-then-immediate sequences, it does not report sequence-specific results, an analysis of period effects, or a carryover assessment. The statistical model and its handling of within-participant dependence are not reported in the registry record.

The study was unmasked. Participants could know whether sensor information was available, and the endpoint includes participant-reported stress and self-care. The record does not describe whether any outcome assessment was blinded or how expectations were addressed. This does not establish that reporting was biased, but it is relevant context for an endpoint based on participant responses.

The registry reports 71 participants monitored during both information periods and planned enrollment of 80, without explaining the difference. The secondary outcome has 57 observations at baseline and follow-up, but the record does not describe the analysis population or missing-data handling. The planned enrollment should not be treated as the number contributing to each reported result.

Finally, the record does not report the original sample-size justification, a full statistical analysis plan, or multiplicity procedures. It lists 11 outcome measures, but only one secondary result is posted. These gaps limit assessment of prespecification, selective reporting, and the strength of secondary inferences.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: LA-CEAL 4.0: Wearable Sensor Project — NCT06086028.
• Registry record last updated 2025-10-20; status last verified 2025-09.
• Results first posted 2025-10-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

LA-CEAL 4.0: Wearable Sensor Project is a completed, randomized, unmasked crossover study sponsored by Tulane University. It examined immediate versus delayed access to information from a wrist-worn sensor among healthcare workers, with stress and burnout listed as conditions of interest.

The primary endpoint was the percentage of days in concordance during the two information periods. The registry reports a mean difference of 0.01 for delayed compared with immediate information, with a confidence interval spanning zero and an unadjusted p-value of 0.773. A secondary burnout-score outcome was also posted, but the record does not report a full analysis plan, missing-data strategy, or multiplicity procedure.

The results are descriptive and uncertain. The registry record does not provide enough analysis detail to assess fully how the crossover structure and incomplete observations were handled.