Hal Morgenstern filed this affidavit in a Metoclopramide lawsuit that alleges a woman developed Tardive Dyskinesia after long term use of Metoclopramide (generic Reglan.) He filed this affidavit because the Reglan attorneys for Wyeth asked to court to exclude Morgenstern’s testimony on the grounds that it was scientifically unreliable under what is known as the Daubert standard.
If you think you might have a Reglan lawsuit, contact me and I’ll put you in touch with an attorney who will work with you to determine if you have a case, and will work to find expert witnesses that can meet the Daubert standard.
NOW COMES the deponent, Hal Morgenstern, Ph.D., and states, under oath, the following:
1. I am over the age of majority, competent to make this Affidavit, and affirmatively state that all matters herein are based upon my personal knowledge.
2. I have reviewed Wyeth's Brief in Support of Motion to Exclude Certain Expert Testimony Under Daubert in this matter. I drafted a response to the arguments and assertions contained in that Brief insofar as they related to my testimony and opinions.
3. A true and accurate copy of the response I prepared in answer to Wyeth's challenge to my testimony is attached hereto. The matters set forth in the attached response are true and accurate to the best of my knowledge and belief.
This the 24th day of August, 2007.
RESPONSE TO WYETH'S BRIEF IN SUPPORT OF THEIR MOTION TO EXCLUDF MY EXPERT TESTIMONY UNDER DAUBERT (filed 7/27/07)
McNeil v. Wyeth
Case No. 3:02-CV-2072-L
Hal Morgenstern, Ph.D.
August 14, 2007
In this document, I respond to Wyeth's motion and supporting brief to exclude my expert testimony in the matter of McNeil v. Wyeth. Many of the points raised by defense counsel are inaccurate, misleading, or irrelevant to their motion. They have taken many of my statements and brief quotes out of contest; they have misunderstood several points that I made in my deposition (on 9/17/04) and report (dated 10/5/04); and they have made scientific or technical errors in their brief.
My comments below are organized around Wyeth's brief. Their specific headings and statements are quoted in bolded italics, followed by my responses.
INTRODUCTION (pp. 1-3)
“Wyeth's motion is a limited one because medical causation is not at issue. Wyeth does not dispute that tardive dyskinesia (‘TD’) may develop in patients treated long-term with metoclopramide (formerly distributed by Wyeth as Reglan(R))….Nor does Wyeth dispute that plaintiff, an elderly woman, more likely than not developed TD from taking metoclopramide for 14 months, over five times longer than the 12-week maximum recommended in the label” (p.1).
In these statements, Wyeth not only emphasizes that causation is not the issue, but they acknowledge that use of metoclopramide (MET) increases the risk of TD (general causation) and that it probably (“more likely than not”) contributed specifically to the plaintiff's condition (specific causation). Despite their stated purpose and these acknowledgments, however, Wyeth devotes most of their brief to the causation issue, attempting to dispute my arguments, which are based on scientific evidence from epidemiologic studies and my own analysis. Their misguided arguments seem to derive from their failure to distinguish adequately between two epidemiologic concepts and objectives: 1) estimating the frequency of TD in a population such as MET users (which is relevant to the warning information on the Reglan(R) label and will be discussed below); and 2) estimating the effect of MET use on the occurrence of TD (which is central to the causation issue). To estimate TD frequency, epidemiologists compute measures such as the prevalence or incidence rate of the condition; to estimate effect, they compute measures of association such as the incidence rate ratio or the risk ratio (relative risk). Since these concepts are critical to my testimony and this response to Wyeth's motion, definitions are previded in Appendix A for relevant epidemiologic measures.
“The issue in this case is the adequacy of the information in the Reglan(R) label. Among other things, plaintiff asserts that the Reglan(R) label is misleading because it understates the risk that long-term users will develop TD. She supports this argument with the testimony of experts who purport to quantify the risk and relative risk of TD with long-term use. Wyeth challenges this testimony because these experts' methodologies do not comport with generally accepted scientific principles and were devised solely for purposes of this litigation” (pp. 1-2).
My report of 10/5/04 dealt entirely with the general causation issue and did not specifically address the adequacy of the warning information in the Reglan(R) label because I was not asked to do so. Because Wyeth's motion to exclude my testimony is based entirely on this issue, I will address the issue in this response.
The general warning in the package insert states that “Extrapyramidal symptoms, manifested primarily as acute dystonic reactions, occur in approximately 1 in 500 patients treated with the usual adult dosages of 30-40 mg/day of metocloproamide. Under the warning for “Tardive Dyskinesia,” no risk or prevalence estimates are provided, but the claim is made that “it is impossible to predict which patients are likely to develop the syndrome.” Not only is this claim inconsistent with the vast TD literature, but the quantitative implication of the warning is unclear. It seems to imply that the risk of TD, another category of “extrapyramidal symptoms,” is extremely low-purportedly less than 1 in 500.
To the best of my knowledge, only one attempt has been made to estimate directly the incidence rate of TD among users of MET. That attempt was made by Wiholm et al. (1984), using Swedish data from 1977 to 1981. For several reasons documented in Appendix B (see Direct Method), however, I believe those results tell us nothing about the incidence rate of TD among long-term users of MET because their estimate of TD incidence was dramatically underestimated–perhaps by 100-fold or more.
Contrary to what is stated several times in Wyeth's brief, I did not claim that we could estimate the risk (cumulative incidence) or incidence rate of TD from a cross-sectional study of TD prevalence. (Rather, I used the results from cross-sectional studies to estimate the effect of MET on TD and discussed various sources of bias in those effect estimates, i.e., to address the causation issue.) Nonetheless, estimates of TD prevalence from cross-sectional studies provide qualitative insight about the validity of the Reglan(R) label. To the best of my knowledge, there are three epidemiologic studies–all cross-sectional–in which the investigators estimated TD prevalence in users of MET and the association between MFT use and TD prevalence.
Ganzini L, Casey DF, Hoffman WF, McCall AI. The prevalence of metoclopramide-induced tardive dyskinesia and acute extrapyramidal movement disorders. Archives of Internal Medicine, 1993; 153:1469-75.
Sewell DD, Kodsi AB, Caligiuri MP, Jeste JV. Metoclopramide and tardive dyskinesia. Biological Psychiatry, 1994; 36:630-32.
Matson JL, Mayville EA, Bielecki J, Smalls Y, Eckholdt CS. Tardive dyskinesia associated with metoclopramide in persons with developmental disabilities. Research in Developmental Disabilities, 2002; 23:224-233.
The first two studies deal with different veteran populations and were discussed in my report of 10/5/04; the latter study deals with adults with mental retardation and was not cited in report of 10/5/04. The investigators of all three studies used reliable and valid examination methods to detect dyskinetic (TD) movements and to diagnose TD. The estimated point prevalence of TD among MFT users was 29% in the Ganzini et al. study and 27% in the Sewell et al. study; the estimated 1-year period prevalence was 40% in the Matson et al. study for both users of MET and users of conventional antipsychotics (see Appendix A for definitions of these measures). If we were to observe a population of MET users in which the true risk of TD is no greater than 1 in 500 (0.2%), as implied by the Reglan(R) label, it would be mathematically impossible for the prevalence of TD to be greater than 25% in that population, given that prevalence depends on the incidence rate of that condition and the mean duration of the condition among cases (see Appendix A, Point Prevalence). Thus, there is no way that the three estimates of TD prevalence could be consistent with a risk of 0.2% unless the investigators of all three studies selected MET users who were known to have TD before their inclusion in the studies. Such a scenario would be a serious violation of scientific as well as ethical principles, and there is no evidence that such violations occurred.
To obtain a quantitative estimate of TD risk in MFT users without directly comparing prevalence and incidence as done above, we can use the indirect method described in Appendix B. This method involves combining results from three sources: 1) my meta-analysis of the results from Ganzini et al. (1993) and Sewell et al. (1994); 2) my published meta-analysis of 21 studies examining the association between antipsychotic use and TD prevalence (Morgenstern et al., 1987); and 3) results from published studies of TD incidence during the first several years of exposure to conventional antipsychotic medications. Although this approach was devised to address the specific warning-label issue in this cas??, it is based on standard methods used in the peer-reviewed epidemiologic literature; i.e., comparing the estimated effects of two exposures on the occurrence of one disease, using the prevalence odds ratio in cross-sectional studies to estimate exposure effects combining results across studies designed to estimate an exposure effect, and using incidence rates to estimate risk. Contrary to the statement in Wyeth's brief (p. 3). I did not assume “that metoclopramide has the same [pharmacological] propensity to cause TD as antipsychotics;” rather, I compared the estimated effects of the two drugs, using epidemiologic findings from peer-reviewed articles.
As shown in Appendix B, the risk of TD among persons treated with MET depends on the age of the persons being treated ??nd the duration of treatment. Because the plaintiff was 66-67 years old while being treated for 14 months with MET, the estimated risk for someone like the plaintiff was somewhere between 6% (1 in 17) and 15% (1 in 7) (refer to the latter two tables in Appendix B). Therefore, my best estimate of D risk for a 66-year old adult treated for one year is much greater than 0.2% (1 in 500). Furthermore, my findings and interpretation are consistent with Pasticha et al. (2006), who concluded that TD risk is “grossly underestimated in the package insert.
TERMINOLOGY (pp. 3-7)
To support their arguments in this case. Wyeth provides several “definitions” of epidemiologic concepts, citing the Reference Manual on Scientific Evidence (Green et al., 2000). I would like to point out that some of these definitions are vague, and three are wrong, according to the peer-reviewed literature in epidemiology and biostatistics. Specifically:
a) The prevalence odds ratio is not “[t]he ratio of the prevalence rate in the group taking the drug divided by the prevalence rate in the unexposed group” (p. 4). That measure is the prevalence ratio. The prevalence odds ratio is the odds of being ?? case in one group (e.g., the exposed) divided by the odds of being a case in a comparison group (e.g., the unexposed) (Rothman & Greenland, 1998, p. 64; see also Appendix A)
b) The relative risk is not the same as the incidence rate ratio (p. 5) Thus, the “relative risk” is not “the ratio of the incidence rate in the population taking the drug divided by the incidence rate in the population not taking the drug.” Because the incidence rate and risk are different concepts, the risk ratio or relative risk is the ratio of two risks, and the incidence rate ratio is the ratio of two incidence rates (Rothman & Greenland, 1998, pp. 237, 242; see also Appendix A)
c) Statistical significance or the p value is not “the probability that a result is simply due to chance rather than an identifiable factor” (p. 6). The p value is the probability of obtaining the observed result (e.g., rate ratio = 2) or a more extreme value (e.g., rate ratio > 2 or < 0.5) if the null hypothesis (rate ratio = 1) were true. Furthermore, reporting statistical significance–i.e., the practice of designating p values less than 0.05 as “significant” and those greater than 0.05 as “not significant”–is generally counterproductive and misleading (Rothman & Greenland, 1998, pp. 183-194; see also Appendix C).
ARGUMENT (pp. 7-20)
B. Dr. Thompon and Mr. Stewart's Opinions About Risk are Ureliable (pp. 9-12)
Wyeth argues that the testimony of these two witnesses must be excluded because they incorrectly equated prevalence estimates in the cross-sectional studies of Ganzini et al. (1993) and Sewell et al. (1994) with estimates of TD risk. They further state:
“…Even plaintiff's own epidemiologist, Dr. Morgenstern, concedes that Dr. Thompson and Mr. Stewart are mininterpreting Ganzini and Sewell” (p. 10).
In fact, I am not familiar with the testimony of those two expert witnesses, and I was not asked about their testimony. Thus, I did not comment on their methods, interpretations, or opinions; and I have no way of knowing whether they correctly or incorrectly interpreted published findings. I was simply responding to the questions asked of me by defendant's attorney (quoted on p. 10).
C. Dr. Morgenstern's Opinions About Risk are Unreliable (pp. 12-19)
Despite the heading of this long section, most of it does not deal with my assessment of TD risk among users of MET or with its relevance to the Reglan(R) label (see above and Appendix B). Instead, it deals with my assessment of whether, and to what extent, MET exposure increases the risk of TD, i.e., the causation issue, which Wyeth concedes in the introduction to their brief. Nonetheless, I will still respond to several misleading and inaccurate point raised in this section.
“After admitting that Dr. Thompson and Mr. Stewart misinterpret the results of Ganzini and Sewell studies, Dr. Morgenstern proceeds to do the same thing– i.e., he purports to use the Ganzini and Sewell prevalence data to quantify the extent to which long-term metoclopramide use increases the risk of developing TD” (p. 12).
I did estimate the effect of MET use on the incidence rate of TD, using the results of two cross-sectional studies; but I did not do the same thing of which they accused Thompson and Stewart–i.e., I did not misinterpret TD prevalence as risk. What I did is use the prevalence odds ratio to approximate the incidence rate ratio, comparing MET users with nonusers, which is common practice in the analysis of cross-sectional studies. The basis for this method is that, assuming no bias, the prevalence odds ratio estimated in a cross-sectional study will equal the incidence rate ratio expected from a cohort study of the same source population (Rothman & Greenland, 1998, p. 64) In my report of 10/5/04, I estimated the incidence rate ratio to be 2.24 (95% confidence interval = 1.07, 4.70; p = 0.033). I then devoted considerable attention to assessing various sources of bias and other methodologic limitations, including temporal ambiguity, selection bias, the effects of risk factors vs. prognostic factors, confounding by unmeasured risk factors for TD, lack of a dose-response association, the high TD prevalence in nonusers of MET, and lack of generalizability. I conclude that, despite these methodologic limitations, use of MET for more than 12 weeks probably does increase the risk of TD; and, although some bias is likely, my estimate of the incidence rate ratio is more likely to b an underestimate than an overestimate.
1. Dr. Morgenstern's Flawed Methodology (pp. 13-16)
(a) Step One: Guesstimate “odds ratios” and ignore their statistical insignificance (pp. 13-14).
I did not “guesstimate” anything. Using standard quantitative methods described and illustrated throughout the peer-reviewed literature. I estimated the prevalence odds ratio, which was clearly defined in my report and in Appendix A of this document. The issue of statistical significance is addressed later and in Appendix C.
“…A true ‘odds ratio’ is a measure of risk that is determined from a type of epidemiological study called [a] ‘case-control’ study. It is similar to the ‘relative risk’ determined by a cohort study” (p. 14)
An odds ratio is not a measure of risk; it is a measure of association (see Appendix A) Moreover, it can be estimated from any type of comparative study, including cross-sectional designs.
(b) Step Two: Combine the odds ratios using a for-litigation-only “meta-analysis,” and then apply “inverse-variance weighting” (p. 14).
The method I used to combine results from the two studies by Ganzini et al. (1993) and Sewell et al (1994) was not a special technique created for litigation only. It is a standard meta-analytic method, using inverse-variance weighting (fixed effects), to estimate the common effect of an exposure such as MET use on the occurrence of a disease such as TD (Rothman & Greenland, 1998, pp. 657-668). Wyeth seems to object to my method for combining results from the two studies–not because it violates any principle of meta-analysis–but because it yields a result that they would call “statistically significant” (i.e., p = 0.033, which is less than 0.05). I agree that my effect estimate is not likely to be a chance finding–not simply because the p value is less than the arbitrary cutoff of 0.05, but because of the consistency of results across all three studies that examined this association and because of other supporting evidence.
(c) Step Three: Assume Prevalence Equals Incidence (p. 15).
“…What Dr. Morgenstern is saying when he equates his prevalence odds ratio to relative risk (i.e., the incidence rate ratio) is: ‘Yes they do, if I say so.’ Dr. Morgenstern, however, provides no scientific support or citation for his leap from prevalence to incidence and risk” (p. 15)
As explained earlier. I did not equate prevalence to incidence, nor did I equate the prevalence odds ratio to the incidence rate ratio. Rather, I used the prevalence odds ratio to approximate the incidence rate ratio and considered several possible sources of bias that could distort my result and limit causal inference. Contrary to the claims made in Wyeth's brief, findings from cross-sectional studies are frequently used in this way to estimate effects on nonfatal conditions, as explained by Rothman and Greenland (1998, p. 64) and illustrated throughout the epidemiologic literature. All types of epidemiologic studies can yield biased results; thus, researchers should routinely address these methodologic limitations in their studies and in the studies of others.
(d) Step Four: Generalize (p. 15)
“…Ganzini and Sewell studied small, atypical populations of chronically ill, elderly, mostly male military veterans with a grossly inflated background rate of TD…Dr. Morgenstern nevertheless asserts that his results ‘probably’ are generalizable to all metaclopramide users. Such guesswork simply does not pass the test of reliability under Daubert” (pp. 15-16).
My assessment of generalizability was not a matter of “guesswork” Generalizing results from one or more studies to other populations is largely a matter of logic and judgment, not simply statistics or sampling (Rothman & Greenland, 1998, pp. 133-134); and generalizability differs for measures of disease frequency and exposure-disease association. I have not attempted to generalize estimates of TD prevalence from the studies of Ganzini et al. and Sewell et al. to other populations because populations can differ considerably in the distribution of TD risk factors such as age; but I have considered the generalizability of effect estimates from those studies, based on epidemiologic principles.
Wyeth seems to be implying that we cannot generalize the estimated MET-TD association obtained from the two studies of veterans to other adult populations in which MET might be prescribed. For such lack of generalizability to hold, however, there must exist certain TD risk factors that strongly modify the effect of MET use on TD risk, and the distribution of these effect modifiers would have to differ appreciably between veteran and non-veteran populations. In fact, from my knowledge of the TD literature (which I have been studying for 27 years), I know of no risk factors that would satisfy these conditions (often called “interactions”) for either MET or antipsychotics. To place this issue in context, consider the well-known VA study in which the investigators found that coronary bypass surgery increased survival in patients with stable angina and three-vessel coronary artery disease (VA Coronary Artery Bypass Surgery Cooperative Group, 1984). Despite restriction of this study population to veterans, the results helped shape treatment decisions in non-veteran populations as well. Furthermore, the findings of Matson et al. (2002) from their study of adults with mental retardation are consistent with the results of the two veteran studies. Thus, although the findings presented in my report should be replicated in other populations, I have no reason to expect the results to be substantially different. Moreover, none of the points raised by Wyeth in their brief are sufficient to negate the generalizability of these findings.
Two additional points should be noted in regards to the issue of generalizability. First, lack of generalizability does not represent a type of bias in estimating exposure effects. These are different issues with very different implications to the interpretation of results. Second, in my estimation of TD risk among MET users (see Appendix B, Indirect Method), I did not generalize TD risk from veterans to the general population. Rather, I extrapolated TD risk from regular user of conventional antipsychotics among outpatients of different ages. Of course, we cannot be sure how well the background TD risk in these psychiatric populations (in the absence of antipsychotic use) reflects the background risk in the general population of MET users, but this issue cannot be addressed without conducting large comparative studies of TD incidence in multiple populations of MET users and nonusers.
2. Dr. Morgenstern's Methodology is Unreliable (pp. 16-19)
(a) Dr. Morgenstern ignores generally accepted standards governing epidemiology when offering his litigation opinions.
“The most basic problem with the reliability of Dr. Morgenstern's risk opinion is that it is not keeping with the well established principles governing the discipline through which he purports to derive it. Nor is it in keeping with his own non-litigation standards; that is, when he is an expert witness as opposed to a scientist, Dr. Morgenstern uses methodology he would not employ outside the courtroom. Specifically, when he is writing for his peers outside the litigation context, he expressly acknowledges the limitations of prevalence data:
Perhaps the greatest limitation of the studies included in this [meta] analysis is that they are all cross-sectional. Thus, we cannot determine from the data alone to what extent neuroleptic exposure increased the risk of [tardive dyskinesia] or affected the course of the disease among cases” (p. 16) (quoted from Morgenstern et al., 1987, p. 722).
The accusation made in these statements by Wyeth is completely false. The principles and standards that I applied in my 1987 peer-reviewed paper are exactly the same as the ones I have been applying in this case. The purpose of that 1987 paper (which was used and cited in Appendix B) was to conduct a meta-analysis of 21 cross-sectional studies that examined the association between the use of conventional antipsychotics and TD prevalence. By combining results from these studies, I found an overall odds-ratio estimate of 2.87 (95% confidence interval = 2.34, 3.52). The limitation of using cross-sectional studies quoted above is the same point that I made in my report of 10/5/04 in this case. In particular, I discussed in my report three methodologic limitations of cross-sectional designs: temporal ambiguity; possible selection bias; and the difficulty in distinguishing between the effect of MET use on disease risk and its effect on the course of disease including its duration. It is this latter point that is noted in the above quote from my 1987 paper. Furthermore, I should point out that our conclusion from that 1987 meta-analysis of cross-sectional studies–that long-term use of conventional antipsychotics is a risk factor for TD–is now widely accepted by researchers and practitioners.
(b) Dr. Morgenstern's methodology has not been published or subjected to peer review and was generated solely for this litigation.
“Dr. Morgenstern would not even try to publish his prevalence-to-incidence use of Ganzini and Sewell; he testified that “I have no intent–it never even occurred to me that I would publish this” (p. 17).
This accusation is both false and misleading. In fact, as noted above, I did publish a paper in 1987 with a similar objective and approach (based on cross-sectional studies) as those used in my report for this case. My statement about not intending to submit my findings in this case to a peer-reviewed journal is taken out of context; in no way does this statement mean that I regard my methods or interpretations in this case to be professional substandard. Although I use results from my previous studies to support expert testimony in litigation cases, I have never used my testimony in such cases to prepare articles for peer-reviewed journals. Moreover, having served as an associate editor and reviewer for several professional journals. I do not think there would be much interest in publishing a meta-analysis of only two studies, especially in light of the fact that similar conclusions have been previously published by others in peer-reviewed journals (e.g., Jiménez-Jiménez et al. 1997; Lata & Pigarelli, 2003).
(c) Dr. Morgenstern scoffs at measuring the rate of error through statistical significance.
“One cannot evaluate the rate of error of Dr. Morgenstern's prevalence-to-incidence methodology because he does not believe that ‘what you call statistical significance has any scientific meaning. In other words, Dr. Morgenstern does not acknowledge the legitimacy of the generally accepted method for determining whether the results of epidemiological studies mean anything, terming it ‘fallacious.’ But if the concept of statistical significance is discarded, there is no way to tell if a particular result is meaningful except through ‘ipse dixit’ of the expert” (p. 18)
Contrary to Wyeth's statements, I have no objection to the derivation of p values for testing the null hypothesis of no association. Indeed, I reported the p values for the MET-TD associations in the studies of Ganzini et al. ( p = 0.083) and Sewell et al. ( p = 0.085) and in my combined analysis of those studies ( p = 0.033). These p values reflect the extent to which the null hypothesis is compatible with observed results; but they are not, as stated by Wyeth, “the probability that a result is simply due to chance” (p. 6; see also my comments under TERMINOLOGY). Such misunderstanding of p values often leads to misinterpretation of statistical results, and this problem is made worse by the practice of designating p values less than 0.05 as “significant” and those greater than 0.05 as “not significant.” This practice is counterproductive and misleading, as explained in Appendix C, and it is now strongly discouraged by contemporary researchers (e.g., see the citations for 7 textbooks in Appendix C)
Thus, we cannot assess “whether the results of epidemiological studies mean anything” by determining whether the p value is < or > 0.05 (or equivalently whether the 95% confidence interval includes the null value). What we do, unfortunately, is far more complicated than that. In addition to deriving p values, we do a number of things to interpret statistical findings. including the following; assess the precision of our parameter estimates by confidence-interval width; consider possible sources of bias (e.g., selection bias, misclassification bias, and confounding), how they are likely to have affected our results, and, when possible, correct for those biases (e.g., adjustment for confounders); consider how the results may or may not be generalized, based on all relevant findings, logic, and prior knowledge of the disease and its natural history; consider findings from animal, cellular, and tissue studies; and consider other issues such as biological plausibility and consistency with other related findings (e.g., regarding similar diseases or exposures).
D. Extrapolation Based on Studies of Users of Antipsychotics is Not Reliable (pp. 19-20)
“Dr. Morgenstern makes reference to the supposed relative risk of TD associated with antipsychotics, which according to his ‘meta-analysis' is 2.9. He compares this figures to his improperly derived 2.24 relative risk figure for metoclopramide, and concludes that the latter must be correct because it is ‘nearly as great as the former.’ This reasoning makes no sense” (p. 19).
Of course this reasoning makes no sense, but it is not the reasoning that I used. I did not conclude that the estimated effect of MFT is correct because it is similar to the estimated effect of antipsychotics on the same disease. What I did was compare the two estimates with each other. The validity of each was assessed separately–for conventional antipsychotics in my 1987 paper and for metoclopramide in my report and in this document.
“Presumable Dr. Morgenstern's comparison is premised on his assertion that metoclopramide is similar to the antipsychotics. He offers this opinion even though he is not a pharmacologist” (p. 19).
I made no assertions or assumptions in my testimony or report that were based on pharmacological knowledge. My comparison of antipsychotics and MET was strictly empirical, based on the results of several epidemiologic studies. Nonetheless, I am aware that MET, in addition to being used as a prokinetic and antiem??tic agent to treat several disorders, is a dopamine receptor antagonist with antidopaminergic properties similar to conventional antipsychotic drugs that are known to cause TD, and that MET has been shown to induce dyskinetic-like movements in pigs (Jeste & Wyatt, 1982; Shaffer et al., 2004; Pasricha et al., 2006). Consequently, the effect of MET on TD in humans is biologically plausible, especially when used for longer periods.
Many of the points raised by Wyeth in their brief are inaccurate, misleading, or irrelevant to their motion. They have taken many of my statements and brief quotes out of context; they have misunderstood several points that I made in my deposition and report; and they have made scientific and technical errors.
Wyeth's motion is primarily based on two claims: 1) no meaningful interpretations can be made about the effect of MET on TD on the basis of results from cross-sectional studies; and 2) my expert opinions are unreliable because they are based on methods and reasoning that are not consistent with modern principles and standards of epidemiologic practice. I believe that I have shown both claims to be false.
My opinions in this case are: 1) use of metoclopramide for more than 12 weeks probably increases the risk of tardive dyskinesia–a point conceded by Wyeth in their brief; and 2) the risk of TD among users of metoclopramide for more than 12 weeks is much greater than 1 in 500, as implied on the package insert–an issue that was addressed only tangentially in Wyeth's brief.
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