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LETTERS TO THE EDITOR |
Multiple Sclerosis Center at University of California, San Francisco, Department of Neurology, University of California, San Francisco, San Francisco, CA 94143-0114
I read with interest the recently published article by Ackerman et al. (1) on the relationship between multiple sclerosis (MS) exacerbations and stress. Although such a relationship has been suggested by several earlier studies, the validity of any association between MS exacerbation and stress has been very difficult to establish with certainty (see 2 for review). Part of the reason for this has been a failure to characterize accurately the nature and severity of the stress and the possible introduction of reporter bias into the data. In their study, Ackerman et al. (1) have attempted to remove these potential sources of bias by using weekly questionnaires and structured interviews. Unfortunately, however, they have also used other methods that have introduced bias and which, I believe, raise serious concerns regarding the validity of the relationship that they propose between stressful life events and MS exacerbations.
First, although the actual numbers are difficult to reconcile from the text, the authors appear to have excluded from analysis a sizable proportion of the life events that they identified. Thus, among the 23 women in this 1-year study, they observed 215 life events or an average of 9.3 events per person per year. They define severe life events as either level 1 or level 2 on their 4-level rating system; by this dichotomization, 99 (46%) of these 215 events were classified as severe, for an average of 4.3 severe events per person per year. In the Methods, the authors state that they excluded from analysis "life events that were potentially related to MS disease activity," and they report in the Discussion that "subjects averaged 1.6 severe events per year and 6.9 total events per year, excluding events directly attributable to MS disease activity." If accurate, this indicates that 63% of the severe events and 26% of the total events were excluded from analysis. Whenever such a large proportion of the data is excluded, it is reasonable to consider whether the method used to exclude data might have introduced bias into the dataset. In the present circumstance, the method used by the authors almost certainly did introduce bias. Thus, presumably, excluded events were exclusively from the postattack period (how else could they consider an event to be caused by MS disease activity?). Also, life events were probably less likely to be considered linked to an MS attack the farther removed the event was from the attack itself. If life events are evenly distributed throughout the year and unrelated to MS attacks (ie, the null hypothesis), this method of excluding postattack events will artificially lower event rate in the immediate postattack period. Over time, this event rate would rise until the next attack, after which it would artificially fall again. For their analysis of the time to previous life event (Figure 1), the authors picked their controls at a "date randomly selected" so as not to be within 6 weeks of the start or end of an exacerbation (ie, between attacks). This means that controls were selected at times expected to be artificially depleted of life events, whereas the dates of exacerbations were picked at times when the event rate was expected to be at its zenith. The bias introduced by this method could easily explain the observations presented in Figure 1. Even if the authors are correct that there might be a bias in the study from life events caused by an MS attack, their method does not really help. In the first place, it is pure conjecture whether an MS attack might increase the likelihood of subsequent life events. In the second place, it is not sensible to remove 1 bias by creating another, especially when the magnitude of neither bias is known.
Second, their analysis using the so-called "fixed-effect partial likelihood" method to calculate hazard ratios from event rates for exacerbations (Figure 2) also appears fatally flawed. For example, although the authors do not fully clarify this method, similar survival methods generally assume that the hazard ratio remains constant (in this case, as reported by the authors, there was an increase of 13.18 in the relative risk of an exacerbation for each unit increase in the rate of life events). However, in the present study, such an assumption of constant hazard ratio is untenable. Thus, although higher event rates often appear to have shorter interattack intervals in Figure 2, the interattack interval for the 5 exacerbations without any antecedent life events (ie, having an event rate of zero events per week) was actually among the shortest found in the study (9.2 weeks). Such an observation is clearly at odds with the notion that lower event rates are consistently associated with longer interattack intervals. Similarly, the longest interattack interval for intervals containing only 1 event was 26 weeks, and the longest for intervals containing only 2 events was 17 weeks. All of the longest interattack intervals (30 weeks) were associated with 4 or 5 events in the interval, as one would expect if the event rate were, in fact, constant over time. Moreover, considering only those observations within the band of interattack intervals between 4 and 15 weeks (and extending across all observed event rates in this study), the frequencies of the actual observations (from 0 to 7 events) fit remarkably well with the expected frequencies from a Poisson distribution with a fixed rate of approximately 
= (61 events/27 exacerbations) = 2.26 events/exacerbation (goodness-of-fit 
2 = 0.37; df = 2; p > 0.8). Importantly, this calculated Poisson rate in the most active patients is actually lower than the crude rate calculated from the entire study cohort of (163 nonexcluded events/60 exacerbations) = 2.72 events/exacerbation. Consequently, the analysis method used by the authors is fundamentally flawed, and the actual observations from the study do not support any proposed relationship between life events and MS exacerbations.
REFERENCES
Western Psychiatric Institute and Clinic, Pittsburgh, PA
Dr. Goodin and his colleagues have made substantial contributions to our understanding of physical and psychological factors that may trigger multiple sclerosis (MS) exacerbations. In particular, their recent review (1) identifies a number of methodological problems in previous MS studies and proposes the need for prospective longitudinal studies. In his editorial letter, Dr. Goodin has critically examined our prospective study of stress and MS exacerbations published in Psychosomatic Medicine (2). Unfortunately, his analyses and conclusions are based on some misunderstandings of the methodology and data analytic strategies we used.
The first concern Dr. Goodin raised was a potential for bias in our analysis comparing the timing of life events before control periods and MS exacerbations. In this analysis, we randomly selected the first day of 1 MS exacerbation per subject, and 1 control date that was not within 6 weeks of the beginning or end of an exacerbation. We then examined the timing from the most recent life event and found a shorter time from stressor to exacerbations compared with the timing from stressor to control dates (14 vs, 33 days, I = 5.03, p < .0001). In his critique, Dr. Goodin accurately noted a reduction in the number of life events we used in this analyses from 215 total life events (average of 9.3 events per year) to 158 life events (6.9 per year), and was concerned that both the size and distribution of excluded events may have biased the results. We did not elaborate on the reason for data reduction in the article, so this is a reasonable assertion. However, the excluded data did not represent life events that were a consequence of MS exacerbations, as Dr. Goodin assumed, but rather represented life events that occurred during MS exacerbations. These events may contribute to the overall length of exacerbations but are not considered potential triggering events. Dr. Goodin’s concern that the reduction in life events could have occurred preferentially during control periods is therefore unfounded, because no data points were excluded in either of the intervals that we compared.
Overall, less than 5% of life events were excluded as a consequence of MS disease activity, and these events generally occurred during MS exacerbations or immediately after the attacks. The reason for their exclusion was to reduce the chance of labeling events as disease-triggering events if they were simply part of a cycle of increasing MS disease activity. For example, a subject might have experienced left-sided weakness during an exacerbation and lost her job as a result of difficulty walking. If this was followed by further development of MS symptoms, we could not be certain that the job loss was a trigger for the subsequent MS symptoms, because the life event might have been embedded in a period of deteriorating physical health. Dr. Goodin is correct in stating that the effect of removing MS-related events is unknown; however, the removal of life events that would otherwise have been labeled as potential triggers of exacerbation is contrary to our hypothesis of a link between stress and MS and is unlikely to produce false-positive results.
In his discussion of this issue, Dr. Goodin also implied that there was a substantial reduction in the number of severe events in the final data set compared with nonsevere events. This conclusion might have been based on a misunderstanding of the Life Events and Difficulties Schedule (LEDS) methodology and the definition of nonsevere vs. severe events. As part of the LEDS technique, all life events are rated using a 4-point scale for both their short-term threat (experienced at the time of the event) and long-term threat (experienced 2 weeks after the event). Classically, the LEDS literature has defined events ranked as 1 or 2 on long-term threat as severe and events ranked as 3 or 4 on long-term threat as nonsevere. As described in the article, 46% of the events were rated as level 1 or 2 on short-term threat, and 23% of the events in the final dataset were identified as severe events. Dr. Goodin concluded that 63% of severe events were therefore eliminated; however, that incorrectly assumes that all events with level 2 short-term threat would be considered severe events. In our study, 43% of level 2 short-term events remained at level 1 or 2 after 2 weeks. Thus, only 24% of the initial life events were considered severe, which did not differ from the 23% of severe events in the final cohort.
The second major concern raised in Dr. Goodin’s letter was the use of the fixed-effect partial likelihood (FEPL) method to examine the relationship between the rate of life events and likelihood of developing an exacerbation. His concerns appear to reflect an incomplete understanding of the statistical method we used, and the alternative analyses he provides have limited value. Dr. Goodin accurately identified a subset of data points in Figure 2 for which the rate of life events was zero and there was a relatively short interexacerbation interval. He therefore concluded that our finding that higher event density was associated with an increased hazard of developing an MS exacerbation is untenable. His concern may have stemmed in part from a misinterpretation of Figure 2, a scatter plot of the relationship between life event density and the period between exacerbations. Unlike standard survival curves, in which each data point represents 1 subject, the scatterplot and FEPL method incorporate multiple data points per subject. In this case, the 5 data points with a life event rate of zero were contributed by a small number of subjects who had relatively active disease but were fortunate enough to have few life events. We would certainly not hypothesize that life events are the only factor that contributes to the timing of MS exacerbations. Thus, the fact that several data points do not fit a standard survival curve is not relevant. The FEPL procedure adjusts for multiple data points per subject in the calculation of hazard ratios and therefore produces valid estimations of the hazard rate in relatively small data sets. Dr. Goodin’s subsequent attempt to divide the data into intervals containing different numbers of life events and then examine the length of time between exacerbations is a less elaborate exploration of the data that does not account for multiple data points per subject or adjust for individual differences in baseline hazard or stable covariates.
Finally, the use of a Poisson distribution to calculate the number of events per exacerbation for the "most active patients" is interesting but does not support Dr. Goodin’s conclusion. He derived a fixed rate of 2.25 events per exacerbation for the active group and compared it with the overall number of events and exacerbations in the data set. Because these numbers were similar, he concluded that there must be no relationship between life events and exacerbations. The error in his analysis is to assume that the lengths of exacerbations are equal. Subjects with more active disease likely spent a larger portion of the study period in exacerbations. Their life events (with events during exacerbation excluded) would be divided into smaller periods such that if the number of life events were evenly distributed, a lower number of events between exacerbations would be expected. Event density therefore more accurately describes the relationship between the presence of life events and exacerbations compared with life event number, and Figure 2 clearly shows an increase in time between exacerbations for event rates below 0.2 events per week.
The article under discussion was an initial exploration of data from our longitudinal study of MS, and the statistical techniques were selected because of their usefulness in examining relatively smaller sample sizes. We have subsequently published a more thorough examination of biological and psychosocial factors that influence MS disease activity in a cohort of 50 women with MS (3). In that analysis (which included all subjects from this study), we used a repeated-measures logistic regression analysis to examine whether the occurrence of life events increased the likelihood of subsequent exacerbations, and found that MS exacerbations were significantly more likely to occur during the 6-week period after life events (parameter estimate = 0.29, z = 3.21, x2 = 10.3, p < .005). Furthermore, hierarchical regression analysis of variables explaining the amount of time subjects were ill with MS symptoms revealed that life event density was an independent predictor of the amount of time patients were ill, even after accounting for disability level, immunomodulatory therapy, and reactivity to an acute experimental stressor.
In conclusion, we share Dr. Goodin’s concern regarding potential bias in the design and analysis of studies of stress and MS. However, the problems he identifies in his letter appear to stem largely from misinterpretations of the data. In our opinion, the largest source of bias in both clinicians and researchers is the tendency of all-or-none thinking regarding the relationship between stress and MS disease activity. It is our hope that we can move past arguments over whether stress influences autoimmune diseases such as MS and begin to identify individual risk factors, mediators, and moderators of this relationship.
REFERENCES
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