Phase 2 Trial of a Nicotinic Agonist in Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 2 Trial of a Nicotinic Agonist in Schizophrenia (NCT00100165), a randomized phase 2 study. The primary outcome is Neurocognitive Performance.

2. Clinical Question

The study hypothesis described in the registry was that DMXB-A could improve attention and other neuropsychological dysfunctions in schizophrenia, with a possible relationship to psychosocial outcome. The posted primary result, however, concerns neurocognitive performance measured as change from baseline; it does not report a measure of psychosocial outcome. The secondary outcome listed is change on the Scale for the Assessment of Negative Symptoms (SANS).

The trial is described as randomized, triple-masked, and crossover. Its posted arm summaries give mean changes for placebo and each dose. The comparisons estimate the difference in mean change between each dose and placebo, but the registry record does not report a sponsor analysis or explain how the crossover structure was handled in an analysis. These results therefore address the posted comparisons as recorded, rather than establishing a complete account of the trial's intended analysis.

3. Trial Design

This was a Phase 2 randomized crossover trial of DMXB-A in schizophrenia. The registry record lists enrollment of 29 and identifies placebo, DMXB-A 75 mg, and DMXB-A 150 mg as the study treatments. The capsules were described as blinded, and each active dose and placebo was taken twice per day. The masking designation was triple. The record does not identify the three groups as separate parallel groups; the stated model is crossover, in which participants can receive more than one condition at different points in a trial.

The posted results report a mean and standard deviation for each condition, each with an arm count of 29. Those counts should be read as the counts reported for the conditions, not added to infer the number of unique participants in a crossover study. The registry record does not report the treatment sequence, period lengths, washout arrangements, or details of how repeated measurements were incorporated into the sponsor's analysis. Those design details matter when interpreting a crossover trial because observations from the same participant are related, and the ordering of treatments can be relevant.

The primary outcome was neurocognitive performance, measured as change from baseline at 1 month. The registry describes six domains: speed of processing, attention/vigilance, working memory, verbal learning, visual learning, and reasoning/problem solving. The scale was the National Institute of Mental Health Measurement and Treatment Research to Improve Cognition in Schizophrenia Neurocognitive Consensus Combined Battery, with a stated range of 0-100 and higher scores indicating better performance. SANS was listed as a secondary outcome, also at 1 month.

The trial is marked completed. Its start and primary-completion entries are 2005-01 and 2007-07. The original design's sample-size assumptions, sequence allocation details, and full statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Subjects were administered 1 week of placebo to assess their ability to comply with BID dosing prior to administration of drug or placebo. There was a 1 week washout period between arms.

Baseline

First Intervention (4 Weeks)

Washout (1 Week)

Second Intervention (4 Weeks)

Analysis population for the primary outcome, as defined in the registry: change from baseline in cognitive performance as measured by a t-test at 4 weeks after taking the drug or placebo

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 Neurocognitive Performance, measured over 1 month.

The primary endpoint is change from baseline in neurocognitive performance, expressed as a t-score change and reported as a mean with standard deviation. The registry describes assessment at 1 month and identifies six domains: speed of processing, attention/vigilance, working memory, verbal learning, visual learning, and reasoning/problem solving. The measure is the National Institute of Mental Health Measurement and Treatment Research to Improve Cognition in Schizophrenia Neurocognitive Consensus Combined Battery. Its stated range is 0-100, with higher scores indicating better performance.

Change from baseline is used to describe how a participant's measured performance differs from the starting assessment over the specified follow-up period. Comparing mean changes between treatment conditions asks whether the average observed change differs between conditions. It does not, by itself, show how individual participants changed, how many improved, or whether a difference is important to patients. A mean can also conceal variation in response across people and across the six domains.

The record says that the domain performance is compared to a normative sample of schizophrenia subjects and that performance is determined and compared to baseline using a t-test. It also describes the outcome as change from baseline in cognitive performance at 4 weeks, while the primary outcome timeframe is listed as 1 month. The registry record does not explain this wording difference. The posted primary summaries report the mean changes and standard deviations for each condition, but do not provide domain-specific results or a breakdown across individual participants.

7. Results Posted in the Registry

• 3-(2,4-dimethoxybenzylidene) Anabaseine 75 mg: mean 6.10 versus 4.50 on control; difference 1.60 (95% CI -2.73 to 5.93), standardized effect d = 0.19; z-test p = 0.469.
• 3-(2,4-dimethoxybenzylidene) Anabaseine 150 mg: mean 7.60 versus 4.50 on control; difference 3.10 (95% CI -1.58 to 7.78), standardized effect d = 0.34; z-test p = 0.195.

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.

Scale for the Assessment of Negative Symptoms (SANS)

• 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:
  • 3-2,4 Dimethoxybenzylidene 75 mg: mean 6.10 versus 4.60 on control; difference 1.50 (95% CI -2.66 to 5.66), standardized effect d = 0.19; z-test p = 0.480.
  • 3-2,4 Dimethoxybenzylidene 150 mg: mean 7.60 versus 4.60 on control; difference 3.00 (95% CI -1.53 to 7.53), standardized effect d = 0.34; z-test p = 0.194.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 3-2,4 Dimethoxybenzylidene 75 mg 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 3-2,4 Dimethoxybenzylidene 150 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome, SANS, with posted mean changes for the two DMXB-A doses and placebo. Across the secondary comparisons, the dose-condition means are numerically higher than the placebo mean, and the recalculated mean differences are positive. The confidence intervals include zero, so the secondary estimates remain compatible with no mean difference as well as with differences in either direction. This overall pattern is similar to the primary neurocognitive comparisons, rather than providing a clearly distinct statistical pattern.

The secondary results are related to, but do not replace, the primary result. They concern a different outcome and should be interpreted on their own scale. The record does not give a definition of the direction or clinical interpretation of higher SANS change scores, so the numerical ordering should not be translated into a claim of improvement or worsening. The secondary summaries also do not provide participant-level trajectories or an account of how the crossover design was handled.

Unadjusted secondary results carry less weight when several outcomes or comparisons may be examined. Considering multiple results increases the chance that some appear notable by chance, even if there is no underlying difference. A prespecified hierarchy or adjustment procedure can address that concern, but the registry record does not report a multiplicity plan or adjusted secondary analyses. It also lists no reported analyses. The secondary findings are therefore best treated as descriptive and exploratory, rather than as independent confirmation of a treatment effect.

The appropriate overall reading is that the posted secondary summaries do not resolve the uncertainty in the primary outcome. Their broad direction resembles the primary comparisons, but their uncertainty and the absence of a reported analysis plan limit how much evidential weight they can add. They are useful context for the outcome pattern, not a basis for a separate efficacy conclusion.

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

• Scale for the Assessment of Negative Symptoms (SANS)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

A mean difference compares the average change in one condition with the average change in another. For the primary outcome, placebo is the reference condition and each DMXB-A dose is compared with it. A positive posted difference means the treatment-condition mean change is numerically higher than the placebo mean change. Because the scale is described as having higher scores for better performance, direction can be described in that scale's terms; it does not establish that the difference is reliable, important, or caused by treatment.

The posted primary comparison for 75 mg is a mean difference of 1.6, and for 150 mg it is 3.1. These are unadjusted recalculations from the reported means and standard deviations. A crossover trial ordinarily raises questions about within-participant pairing and treatment period, because the same participant may contribute observations under more than one condition. The registry record does not report the sponsor's analysis or enough detail to determine how pairing, sequence, or period effects were treated. The recalculations should therefore be read as comparisons based on the posted summaries, not as a replacement for a fully specified crossover analysis.

What does the standard deviation tell us?

A standard deviation describes how spread out observations are around their mean. Larger spread means participant-level changes vary more widely. The primary standard deviations are 7.3 for placebo, 9.4 for 75 mg, and 10.6 for 150 mg. They are distinct from standard errors and confidence intervals: a standard deviation describes variation among observations, while a standard error describes the uncertainty in an estimated mean or contrast. The posted summaries do not provide individual-level values, so the distribution shape and possible outliers cannot be assessed.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the estimate under the statistical method used. It conveys precision as well as direction: a narrower interval is more precise, while a wider interval leaves more plausible values unresolved. For each primary comparison, the 95% interval includes zero. Zero represents no mean difference between conditions. The intervals also extend to positive and negative values, so the posted estimates do not precisely distinguish a difference favoring one condition from no difference or a difference in the other direction. A confidence interval is not a probability statement about the true effect being inside that particular interval.

What does a p-value contribute?

The unadjusted p-value measures how unusual the observed data, or more extreme data, would be under a model in which the compared means have no difference. It does not give the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The primary p-values are 0.469 for 75 mg versus placebo and 0.195 for 150 mg versus placebo. They are unadjusted and should be considered alongside the effect estimates and confidence intervals, not interpreted in isolation.

Why does the crossover design matter?

In a crossover design, participants can contribute measurements under more than one treatment condition. These measurements are usually related within a person. An analysis that uses that relationship may differ in precision and interpretation from a comparison that treats conditions as independent groups. Period, sequence, and carryover considerations may also be relevant. The registry lists the trial model as crossover but does not report the treatment sequence, period-specific summaries, washout details, or the sponsor's model. The posted recalculations use arm summary statistics and are unadjusted; they cannot resolve those design-specific questions.

What is meant by planning assumptions?

The sample-size illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. Such calculations answer a conditional planning question: under those assumptions, how many participants per arm would be needed to have a specified chance of detecting that effect by the chosen test? They do not establish that the assumptions match the original trial design. The original sample-size justification and its assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is about how tightly an estimate is determined by the data and statistical method. For the primary comparison of DMXB-A 75 mg with placebo, the mean difference is 1.6 and the 95% confidence interval is -2.732 to 5.932. For 150 mg versus placebo, the mean difference is 3.1 and the interval is -1.584 to 7.784. Each interval includes zero, so neither estimate precisely rules out no mean difference. Each also includes values on both sides of zero, leaving uncertainty about direction as well as magnitude.

The intervals are wide relative to the point estimates. This means that the posted summaries are compatible with a range of possible mean differences, rather than concentrating closely around a single value. The standard deviations—7.3 for placebo, 9.4 for 75 mg, and 10.6 for 150 mg—also indicate variation in the observed change scores. The confidence intervals, not the standard deviations, express uncertainty about the comparisons.

These intervals come from unadjusted recalculations based on the posted summary statistics. The registry record does not report sponsor analyses or details needed to assess a crossover-aware analysis. The intervals should therefore not be treated as a definitive account of the trial's planned inferential method. In particular, the record does not show whether within-participant relationships or treatment periods were incorporated in the sponsor's original analysis.

A confidence interval is not a range containing a fixed proportion of participants, and it is not a direct probability that the true difference lies within its endpoints. It is a method-based way to express uncertainty around an estimate. Here, the intervals indicate that the posted comparisons are not precise enough to establish a clear difference, but that uncertainty is not evidence that the conditions have exactly the same effect.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations, not a count of participants observed in the trial. For these continuous-outcome comparisons, the figures refer to participants per arm, not total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design that, under the stated assumptions and effect size, would have an 80% chance of rejecting a no-difference hypothesis when that specified effect is present. The 90% power column describes the corresponding planning target for a 90% chance. These are prospective design concepts, not the probability that the posted result is true and not a measure of the quality of the completed trial.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect use progressively smaller target effects. Smaller effects need more participants to distinguish them from random variation with the same planned power and significance level. Accordingly, the figures rise as the target effect is reduced. The illustrations use the observed effect as an input, so their values should not be treated as an independent estimate of the effect that a future study will find.

This is not observed power. Observed power is not a substitute for interpreting the estimated difference and its confidence interval. The more informative reading of the posted comparison is the size and uncertainty of the estimated effect, considered with the limitations of the registry's reporting and the crossover design.

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 = 1.600; pooled standard deviation σ = 8.416.
2. n = 2 × (1.96 + 0.842)² × 8.416² / 1.600² = 434.3, rounded up to 435 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 <- 1.6                      # observed difference in means
sigma <- 8.41575902696839                     # 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(100165)
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 = 435 (80% power), 582 (90% power)
 75% of observed effect: n per arm = 773 (80% power), 1,034 (90% power)
 50% of observed effect: n per arm = 1,738 (80% power), 2,326 (90% power)
power.t.test: 435.3 
Simulated power at n = 435 per arm: 0.804 (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 lists a primary neurocognitive outcome and a secondary SANS outcome, with dose comparisons against placebo. Testing more than one outcome or comparison creates a multiplicity issue: the more statistical questions considered, the greater the chance of obtaining an apparently noteworthy result by chance. A prespecified primary outcome, ordered testing strategy, or statistical adjustment can help control that risk. The registry record does not report a multiplicity strategy, a hierarchy among comparisons, or adjusted p-values. The recalculated p-values are unadjusted and should be read accordingly.

The record reports no sponsor analyses. It therefore does not provide a complete account of the primary or secondary analysis methods, the estimand, covariate adjustments, handling of repeated measures, or criteria for inclusion in each analysis population. The trial is described as crossover, but the record does not report whether the analysis used within-participant pairing or accounted for treatment sequence and period. Those details affect interpretation and precision.

Missing-data handling is also not reported in the registry record. The posted summaries give counts of 29 for each condition, but this does not explain whether all randomized participants contributed complete outcome data, how missing measurements were handled, or whether the reported counts refer to the same analysis population across conditions. In a crossover study, data can be incomplete for one condition while available for another; aggregate counts alone cannot show how such cases were treated.

The record does not report interim analyses, stopping rules, protocol deviations, or sensitivity analyses. These details should not be inferred from the completed status or the posted summaries. Without them, readers cannot assess whether the posted results follow a prespecified statistical plan or how robust they are to alternative analysis choices. This absence of reporting is a limitation in interpreting the statistical evidence, not evidence that any particular procedure was or was not used.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: nervousness (31.0%), hallucinations (31.0%), delusions (31.0%), headache (20.7%), restlessness (20.7%).

The registry's serious-adverse-event summary lists 29 at risk and 29 affected for DMXB-A 75 mg, 29 at risk and 29 affected for DMXBA 150 mg, and 29 at risk and 29 affected for placebo. These are the figures as recorded for the conditions. Because the study is crossover, the condition counts should not be added to infer a number of unique participants. The other-adverse-event counts list 29 at risk and 0 affected for each condition.

The listed serious-event terms include nervousness, hallucinations, and delusions, each reported as 31.0%, and headache, restlessness, and tinnitus, each reported as 20.7%. These percentages are event-term entries in the registry summary; they do not establish that the events were caused by a treatment or that the listed terms occurred only in one condition. The registry record does not provide a comparative statistical safety analysis or details that link each event to treatment exposure.

Deaths are not reported in the registry record. Serious-event counts should be read as registry reporting, not as a causal comparison or a complete safety profile.

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

The posted results show positive mean changes in neurocognitive performance for placebo and both DMXB-A doses, with higher condition means for the active-dose summaries. The unadjusted mean differences versus placebo are positive, but their 95% confidence intervals include zero and extend to values on both sides of it. The statistical evidence is therefore uncertain about the size and direction of the underlying mean difference. The results do not establish that either dose improves neurocognitive performance, and they do not establish that the treatments have identical effects.

The trial's stated hypothesis concerns attention and other neuropsychological dysfunctions, while the posted primary measure combines six cognitive domains. The reported means cannot identify which domain, if any, accounts for the overall pattern. Nor do they show how many participants had changes in a particular direction, how durable any change was, or whether the observed differences were important to participants. The posted endpoint is a measured score change, not a direct report of psychosocial outcome.

The secondary SANS summaries show a broadly similar numerical pattern, but they do not remove uncertainty in the primary result. The registry does not report a multiplicity approach, sponsor analysis, or a detailed crossover analysis. These omissions limit confidence in treating the unadjusted comparisons as the complete trial analysis. The sample-size illustrations are conditional planning exercises based on the observed effects; they are not evidence that the trial had a particular chance of finding an effect.

It is also important to distinguish failure to establish a difference from proof of no difference. The intervals allow a range of values, and the registry's posted summaries do not narrow that range enough to support a definitive conclusion. Any broader claim about clinical benefit, harm, or use would go beyond what these statistical summaries establish. The record supports a cautious account of observed means and uncertainty, not a treatment recommendation.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its crossover design and posted summary comparisons raise distinct questions. In a crossover study, the same person can contribute measurements under multiple conditions, so within-person relationships may be important for estimating differences and precision. The registry identifies the design but does not report the sponsor's analysis, sequence details, or treatment-period handling. That gap makes it especially important to distinguish simple recalculations from a complete crossover analysis.

The record also illustrates why point estimates should be read together with confidence intervals. Both primary dose comparisons have positive mean differences, but their intervals include zero and span values in both directions. A ranking of means alone would omit the uncertainty around that ranking. The standard deviations show that individual changes vary, while the confidence intervals describe uncertainty in the comparison.

Finally, the sample-size illustrations make explicit how planning requirements depend on the target effect. Under the stated planning assumptions, smaller effects require more participants per arm. These calculations can help frame future study planning, but they do not reconstruct the original design rationale or turn the completed trial's results into evidence of observed power. The original sample-size justification is not reported in the registry record.

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 principal limitation is the mismatch between the crossover design and the limited statistical detail in the registry record. It reports condition means, standard deviations, and unadjusted recalculations, but does not report the sponsor's analysis or how within-participant dependence, treatment sequence, and period effects were addressed. The comparison intervals should therefore be viewed as summary-based calculations rather than a documented crossover-model result.

The record does not report the original sample-size justification, missing-data methods, analysis populations, interim analyses, or multiplicity plan. It also does not give domain-level primary results, individual data, treatment-period summaries, or sensitivity analyses. These omissions make it difficult to assess robustness, identify whether the combined cognitive result reflects a consistent pattern across domains, or determine how incomplete observations were handled.

The primary outcome wording refers to a 1 month timeframe and describes measurement at 4 weeks. The registry record does not explain this wording difference. The posted outcomes provide mean changes but do not establish clinical importance or give a participant-level account of response. The SANS direction is not explained in the record, limiting interpretation of its numerical changes.

The adverse-event summary is also limited: it lists counts and event terms but does not provide a comparative safety analysis or establish causality. Deaths are not reported in the registry record. These reporting limits should not be filled by assumptions about the protocol or trial conduct.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase 2 Trial of a Nicotinic Agonist in Schizophrenia — NCT00100165.
• Registry record last updated 2020-01-29; status last verified 2020-01.
• Results first posted 2020-01-29.
• 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

This completed Phase 2 study is recorded as a randomized, triple-masked crossover trial of DMXB-A 75 mg, DMXB-A 150 mg, and placebo in schizophrenia. The registry lists enrollment of 29, with twice-per-day blinded capsules and outcomes assessed at 1 month.

The primary outcome was mean change in neurocognitive performance across six domains. The posted dose-versus-placebo mean differences are positive, but both unadjusted recalculated confidence intervals include zero and are broad. The secondary SANS comparisons have a similar broad pattern and are also uncertain. The registry record does not report sponsor analyses, a multiplicity plan, missing-data methods, or details of crossover analysis.

Sample-size figures are planning illustrations under stated assumptions, not observed power. Safety summaries list serious-event counts and terms; deaths are not reported in the registry record. Overall, the posted summaries describe outcomes but do not provide enough statistical detail for a definitive interpretation of treatment differences.