Monday, February 05, 2007

Pathological gambling associated with dopamine agonist therapy in Parkinson’s disease1 - A Closer Look

The above study was published in Neurology in August of 2003, in conjunction with its unveiling at the 55th Annual Meeting of the American Academy of Neurology (AAN). This unveiling came complete with press conferences with lead author, Dr. Mark Stacy, and a press release issued by the AAN and picked up by Reuters.

The authors report that in a retrospective database review of all patients seen at the Muhammad Ali Parkinson Research Center (MAPRC) between May 1999 and April 2000, they found “nine patients with pathologic gambling associated with chronic high dose dopamine agonist (DA) therapy.”


The component parts of the study's central assertion are as follows:

1) timeframe for data collection
2) nine patients
3) pathologic gambling
4) an association
5) chronic high dose dopamine agonist (DA) therapy

And I have found that a closer look at each of these component parts raises quite a few questions. For example, what is the reason for shift in the data collection time period between the first presentation of this data in abstract form in 2000 and its published form in 2003? Likewise, why was there one more patient in 2003 than there had been in 2000, and even more confounding, which patient was it that had been added? Then we encounter the fundamental questions - by what measure(s) are the authors identifying pathologic gambling and the presence of an association? And finally, how can they possibly characterize the drug regimens in question as chronic high dose DA therapy, given the data provided?

When this study was published in 2003, the authors presented nine patients - seven men and two women – in support of their assertion. However, this was not this data’s first exposure. Two of the final three authors submitted the same findings in abstract form to the 6th International Congress on Parkinson’s Disease and Movement Disorders in June of 2000. The conclusion presented was largely the same, but there was one immediately obvious difference in the data presented - there were only eight patients in 2000 - seven men and one woman. Seven of the eight patients in 2000 and eight of the nine patients in 2003 were taking pramipexole.

I have been told by a clinician/researcher that there can be legitimate reasons for such an addition – indeed, he said that oftentimes data changes between time of submission of an abstract to a conference and the time the data is actually presented at the conference, and that it could change again between the conference presentation and the publication of the completed study.


Nonetheless, it appears there are discrepancies. As I will say again later, if any of the authors would like to educate me on the validity of their claim, I am all ears. I have tried going to the mountain, i.e., I have emailed the lead author asking for clarification. He chose not to respond. I have invited each of the authors of this study to read this post and asked for their feedback, input, and corrections – maybe the mountain will come to me.

The complexities of the shifting timeframes put forth as those in which the data was collected for these publications raise many questions for me. In the abstract that would have had to have been submitted by Feb 8, 2000 to meet the deadline for submission, the authors made reference to data that had been collected over a 12 month period – which, presumably, could not have ended later than the date of submission of the abstract, i.e., February 8, 2000 and therefore could not have begun later than February 9, 1999.

However, when the paper was finally published in 2003, the timeframe in which the data was collected had shifted forward almost three months – beginning May 1, 1999 and ending April 30, 2000, That would have to mean that at a minimum, data collected for the abstract between February 9, 1999 and May 1, 1999 had been discarded.

Should we conclude that the time that was included in the 2000 abstract but excluded from the 2003 study, February to May 1999, never yielded any gamblers to begin with? If not, wouldn’t it have made sense in the abstract to specify the actual timeframe in which gamblers became known, i.e. May 1999 to February 8, 2000, rather than tacking on several pre-May months to the timeframe?

I don’t know the answers to those questions.


Given the above, perhaps it was pointless for me to try and figure out which of the nine cases presented in 2003 had not been part of the 2000 dataset, since the only way to go about making such a determination would be to assume that the addition of the ninth patient was the only change to the data – everything else would have had to stay exactly the same in 2003 as it had been in 2000. But I figured there couldn’t have been that much change; there might be one or two averages that would be off, but the majority of the changes should indicate the addition of the same case.

So I started with the two incontrovertible pieces of information about the ninth patient – it was a female, and she was taking pramipexole.

At first blush it looked pretty straightforward – there were two women in 2003, Cases 1 and 9, so since the number of women had gone up by one with the addition of the ninth patient, it had to be one of them. They were both taking pramipexole, so that was no help. However, in the 2000 abstract, one person is listed as being on an antidepressant at the time of discovery of the gambling behavior. In the 2003 study, two people are listed as being on antidepressants at the time the behavior was discovered – Cases 8 and 9. Since Case 8 is male, and we have already determined that the ninth patient was female, Case 8 must have been the one on an antidepressant in the 2000 abstract, which would make Case 9 the ninth patient.

Except for one thing – the number of people whose treatment was to switch to another DA did not change from 2000 to 2003 – both the abstract and the published paper cite six patients whose behavior resolved with a switch – and Case 9 is one of the six in the 2003 paper, which would seem to indicate that she was also one of the six in the 2000 abstract, which would knock her out of the running as the ninth patient.

So, I considered the possibility that Case 1, the only other woman, was the ninth patient. After all, perhaps the discovery that one of the original eight was taking an antidepressant had come after the abstract had been submitted to the conference. The theory that she was the ninth got off to a good start with her being female and taking pramipexole, but came to a screeching halt at her treatment. In 2000, two patients were listed as having received counseling as part of their treatment for gambling. The same number of patients is listed in 2003, and Case 1 is one of them, which would seem to indicate that Case 1 was not the ninth patient either.

The table below shows the data that was presented in each publication – 2000 data in the first column and 2003 data in the second column. The addition of the ninth patient changed all of the averages, of course, but since only the averages were provided in the 2000 abstract, as opposed to each individual’s data as was provided in the 2003 study, it is necessary to extrapolate the data profile of the ninth patient based on the differences between the averages presented in 2000 vs 2003. In doing that, as I said earlier, I made the assumption that the only change to the data was the addition of the ninth patient.

None of the nine cases detailed in 2003 comes anywhere near fitting the data profile I have extrapolated for the ninth patient.

It is interesting to note that, according to the data, the ninth patient was taking more than twice the 2000 average dose of pramipexole, i.e., 8mg/day, which bumped the average dose of pramipexole up from 3.6mg/day in 2000 to 4.3mg/day in 2003, thereby bringing the average DA dose more in line with the assertion that “chronic high dose dopamine agonist (DA) therapy” was the culprit, since 4.5mg/day is the maximum recommended dosage of pramipexole.

Also according to the data, the ninth patient was taking less than half the average dose of levodopa, i.e., 400.2mg/day, which bumped the average dose of levodopa down from 943.8mg/day in 2000 to 883.4mg/day in 2003. Levodopa misuse and addiction have been implicated in PG in several studies2, 3, 4, 5 but the fact that every one of the eight cases in 2000 and nine cases in 2003 was also taking levodopa was dismissed as inconsequential.

The closest the authors come to defining what they term “pathologic gambling” is to characterize the gambling in question as “behavior severe enough to cause financial hardship,” which, as it happens, is not a criterion for pathological gambling as defined by the Diagnostic and Statistical Manual of Mental Disorders, Fourth Edition (DSM-IV) (see Wikipedia Pathological Gambling), a definition that is widely accepted and used as a basis for research and clinical practice.

Regarding the presence of an association, while the authors clearly assert that an association exists, they fail completely to delineate what standard or standards of measure they are using to evaluate the presence of an association.

Statistical Significance Implied but Actually Nonexistent
One universally used standard of measure in the research world is statistical significance –a calculation that assesses whether the difference between, for example, the incidences of behavior X among those exposed to and those not exposed to a particular drug is large enough that it is unlikely to be due to chance.

Among the people taking dopamine agonists in this study, the authors find an incidence of pathological gambling among those taking specifically pramipexole of 1.5% (eight out of 529) and of 0.3% among those taking pergolide (one out of 331). By comparing that incidence to the incidence of PG in the general population, which they cite as being 0.3%-1.3%, when they have already asserted in the title of the paper that an association exists, they effectively create the impression that those numbers indicate the presence of an association, i.e., that an incidence of 1.5% represents a significant elevation from that of the general population – otherwise, why include them, right?

They have not actually said this, however, and if one looks more closely, one might discover why.

The first problem with these numbers is that the authors provide no source for their incidence rate range in the general population. I have looked around quite a bit and the lowest incidence rate I have found is 0.93%6 and that was reported in 1999. There is universal agreement pathological gambling is on the rise, so more current numbers would most likely be even higher.

So, where did the authors find an incidence rate as low as 0.3%? They do not say.

Second, out of curiosity, I used a chi square to calculate the significance of the degree of difference between 1.5% among those taking pramipexole and 0.3-1.3% among the general population. I also had my calculations checked and confirmed by a statistician.

Now, while I cannot explain the mechanics behind chi square, I can tell you that if you plug in two incidences, it derives a number representing the probability that the difference between the two incidences is due to chance. A frequently-used benchmark is 0.05, or 5%, so if the number derived is smaller than 5%, the difference between the two incidences is considered statistically significant. So in this case, the difference between the very bottom of the range for the general population and the incidence found in the pramipexole group, i.e., 0.3-0.4% and 1.5%, the difference is statistically significant; but from 0.41-1.3%, the difference is not statistically significant. As I said, the lowest incidence rate I can find is 0.93%, more than twice 0.4%. Without a source for the range provided by the authors, there is no way to evaluate the validity of those numbers.

As I understand it, if the difference is not statistically significant, one has actually failed to find an association.

A third problem with these numbers is that the sample size of 529 people in total taking pramipexole is probably too small for an incidence rate of 1.5% to be meaningful. From what I understand, and I cannot provide a source because in spite of extensive searching I have not found a resource that defines “large” and “small” sample sizes as they relate to the level of meaning that can be read into the incidence rates found in them, 529 is not a large enough sample size for 1.5% to be suitable as a basis for drawing any conclusions whatsoever.

And finally, it is interesting to note that the incidence of PG among those taking pramipexole in 2000, i.e., seven out of 529, is exactly 1.3%, which is the upper end of the range provided for the general population three years later. The addition of the ninth patient, who, as it happened, was taking pramipexole, brought that incidence up to 1.5% (eight out of 529).

So the question remains – if valid, definitive conclusions cannot be drawn based on the numbers they provide, then by what standard of measure do the authors conclude that an association exists?

Temporal Association Implied but Not Supported
The authors suggest that the presence of an association can be read into the temporal coincidence between the onset of the behavior and an increase in DA dosage – they make a point of saying that seven out of nine of those who gambled started within a month of undergoing an increase in their DA dosage, which gives the impression that they are using time from dosage increase to onset of behavior as a criterion by which the presence of an association can be detected. It even gives the impression that they have quantified the length of time necessary (a month or less) to indicate an association.

However, if there are seven that gambled within one month, then there are two that did not gamble within one month – on what basis are they included? The authors don’t say.

But if one removes two people from the DA/PG data pool of nine total, and if one assumes that one of the two being removed was taking pramipexole and the other pergolide, the incidence rate among those taking pramipexole goes down to 1.3% (eight out of 529); if they were both taking pramipexole, the incidence rate goes down to 1.1% (seven out of 529). We don’t know which it is because the authors don’t provide this information, but either way, removing those two people from the equation blows even the appearance of an increased risk of PG on DAs.

Even the characterization of the allegedly responsible drug regimen is inaccurate. The authors report “nine patients with pathologic gambling associated with chronic high dose dopamine agonist (DA) therapy,” but, as I have already pointed out, they also say that “In seven cases the initiation of gambling occurred within 1 month of increasing the DA dose.”

Well, given that in spite of the recent dosage increases only one out of the nine exceeds the maximum recommended dosage for either DA; four have just been upped to the maximum recommended dosage of pramipexole from an unspecified lower dose; three are still nowhere near the maximum; and the one person on pergolide has just been upped to what might be termed a high dose, the use of the term “high dose” is questionable. It becomes even more questionable when it is paired with ‘chronic,’ given that seven of the nine had only been taking the dose in question for a month at the time that they started gambling.

“GIVEN THE COMPLEX WORLD OF THE PATIENT WITH PD — dopaminergic therapy, chronic illness, and casino availability…”

And so we come to the 2003 study’s conclusion, from which the above headline is a direct quote, believe it or not.

Less comical but equally disturbing is the authors’ closing statement, in which they say that in most of the cases described in the study, excessive gambling appeared to resolve with a dosage reduction. Of the nine cases detailed in the article, however, only one is listed as having resolved with a reduction in dose. Six switched to another DA, an inconsistency that is compounded when one considers that the entire thrust of the study appears to hold DAs in general responsible for the PG.

The assertion that encapsulates the meaninglessness of this study as a whole, however, is this one: "...these subjects illustrate that excessive gambling may occur in advancing PD," a statement that sounds like it is saying something relevant, but actually says nothing at all, given that excessive gambling "may occur" at any time, under any circumstance, and it could happen to anyone.

I could go on, but I probably don’t need to.

Suffice it to say that if each of the component parts of the authors’ central assertion is examined more closely than the average journal reviewer apparently would, and certainly more closely than any of the journalists who swallowed this story hook, line and sinker ever would, the whole premise falls apart. First, there are enough inconsistencies in the transition from eight patients in 2000 to nine patients in 2003 to raise questions about the legitimacy of that change. Second, it is abundantly clear that the authors fail to identify key criteria, namely how they are defining pathological gambling and what standard or standards of measure they are using to identify the presence of an association – it couldn’t be statistical significance because a) there is none, and b) the sample size is most likely too small from which to draw any conclusions; it can’t be temporal coincidence because a) they do not define what length of time qualifies as temporally significant, and b) they include two people for whom they provide zero temporal information, thereby pretty much knocking that out as a potential measure of association. Finally, even their characterization of the drug regimen they say is responsible is inaccurate.

It seems clear to me that the authors fail to support their assertion that they have found an association between DAs and PG. If any of the authors disagree, I would welcome their feedback – I am not interested in thinking I am right when I am not. I am interested in the truth, and in accountability on the parts of researchers, institutions and journals to the people whose lives are going to be affected by what they publish and what they publicize.

1 Driver-Dunckley E, Samanta J, Stacy M. Pathological gambling associated with dopamine agonist therapy in Parkinson's disease. Neurology. 2003 Aug 12;61(3):422-3.
2 Molina JA, Sainz-Artiga MJ, Fraile A, Jimenez-Jimenez FJ, Villanueva C, Orti-Pareja M, Bermejo F. Pathologic gambling in Parkinson's disease: a behavioral manifestation of pharmacologic treatment? Mov Disord. 2000 Sep;15(5):869-72.
3 Gschwandtner U, Aston J, Renaud S, Fuhr P. Pathologic gambling in patients with Parkinson's disease. Clin Neuropharmacol. 2001 May-Jun;24(3):170-2.
4 Serrano-Duenas, M. Chronic Dopamimetic Drug Addiction and Pathologic Gambling in Patients with Parkinson’s Disease Presentation of Four Cases. German J Psychiatry 2002;5:62-66.
5 Avanzi M, Uber E, Bonfa F. Pathological gambling in two patients on dopamine replacement therapy for Parkinson's disease. Pathological gambling in two patients on dopamine replacement therapy for Parkinson's disease. Neurol Sci. 2004 Jun;25(2):98-101.
6 National Opinion Research Center at the University of Chicago. Gambling Impact and Behavior Study: A report submitted to the National Gambling Impact Study Commission. April 1, 1999.

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