QUEENS BENCH DIVISION
Strand, London, WC2A 2LL
B e f o r e :
| XYZ & OTHERS
|- and -
|(1) SCHERING HEALTH CARE LIMITED
(2) ORGANON LABORATORIES LIMITED
(3) JOHN WYETH & BROTHER LIMITED
Mr. Spencer QC, Dr. Powers QC, Mr. Waite QC
and Miss Power (instructed by Arnold & Porter Solicitors) for the 1st and 3rd Defendants
Mr. Underhill QC, Mr. Brook Smith QC and Miss Hamilton
(instructed by Beachcroft Wansbroughs Solicitors) for the 2nd Defendants
Hearing dates : 5th March 2002 31st May 2002
Crown Copyright ©
|The Combined Oral Contraceptive.||6|
|The Regulatory History.||11|
|The Issues in the Litigation.||20|
|B||THE APPROACH TO DECIDING THE FIRST ISSUE|
|Case Control Studies.||27|
|Point Estimates and Confidence Intervals.||36|
|Aggregation of COC Products.||45|
|C||THE WHO STUDY|
|An a Priori Hypothesis?||59|
|All Centres or Oxford?||64|
|Hospital or GP Controls?||68|
|D||THE TNS: THE FIRST TWO STUDIES|
|The Origins of the Study.||81|
|The Progress of the Study.||84|
|The Mercilon Anomaly.||98|
|Duration of Use.||106|
|E||TNS3 AND THE COX REGRESSION ANALYSIS||121|
|The Pill Calendar Data.||127|
|The Attack on Cox by Walker.||133|
|Walker's Separate Algebraic Attack.||158|
|Conclusion on Cox.||159|
|F||THE JICK v FARMER DEBATE||164|
|The UK GPRD.||165|
|The Methods and Findings of the Studies.||171|
|The Development of the Issues.||185|
|Jick V: The Attack on Farmer's Controls.||194|
|G||THE OTHER STUDIES|
|Farmer 2000 "Pill Scare".||255|
|H||BIAS AND CONFOUNDING||258|
|Conclusions on Prescriber, Diagnostic and Referral Bias.||286|
|Hidden Bias and Confounding.||287|
|Conclusions on Bias and Confounding.||288|
|Industry Funding Bias.||298|
|The Bradford Hill Criteria.||302|
|J||OVERVIEW OF THE STUDIES||309|
|K||CONCLUSIONS ON THE FIRST ISSUE||339|
Mr Justice Mackay:
SECTION A: INTRODUCTION
This is the trial of seven lead claims in group litigation against three drug companies in respect of their products. There were at the last count 99 claims currently in being. 40 are brought against Schering Health Care Ltd (Schering), 46 against Organon Laboratories Ltd (Organon) and 13 against John Wyeth and Brother Ltd (Wyeth). All the Claimants took on prescription different brands of the Combined Oral Contraceptive (COC) and say they have suffered various cardio-vascular injuries as a result. Their injuries come under the collective description of Venous-thromboembolism (VTE). The commonest forms of this are Deep Vein Thrombosis (DVT) and Pulmonary Embolism (PE). Some claimants have suffered Cerebral Venous Thrombosis (CVT) and some have suffered from strokes.
(i) Carol Townsend. She was born on the 28th December 1970 and was first prescribed Schering's COC Femodene by her General Practitioner in November 1991. She was then just under 20. On the 20th August 1993 she suffered a DVT. She has continued to suffer leg pain and loss of mobility and has needed help in the home from her sister.
(ii) Debra Jones was born on 23rd August 1970 and was first prescribed Femodene in August 1991 when she was 21. She suffered a CVT on the 4th December 1994 when she was just over 24. She has suffered from very severe headaches, despite repeated lumbar punctures, with nausea and giddiness. Her working ability and social activities are both restricted.
(iii) Andrea Massey was born on the 24th September 1976 and was first prescribed Femodene in June 1995 when she was 18Ύ. On the 23rd July 1995 she suffered a stroke as a result of a paradoxical embolism a very short time after starting on the product. I do not as yet have full details of her current symptoms.
(iv) Karen Roberts was born on the 9th June 1962 and was first prescribed Femodene in January 1995 when she was 32. On the 8th August 1995 she suffered a DVT seven months after that first prescription. She has a swollen left leg, her walking is limited and she has an increased risk of recurrence of VTE.
(v) Jacqueline Diplock-Webb was born on the 2nd January 1958 and was prescribed Organon's product Marvelon in March 1993 having also been prescribed it in 1983 and 1985. On 29th August 1993 when she was just over 25½ she suffered a DVT. She has a constant ache in her leg made worse by walking and climbing stairs.
(vi) Nicola Moores was born on 14th February 1967 and was prescribed Organon's product Mercilon in September 1990 when she was 23. In November 1993 and again in August 1995 she suffered episodes of PE she then being 26 and 28. She has had episodes of chest pain and dyspnoea. She has suffered a severe loss of confidence and is worried by the thought of a recurrence of PE.
(vii) Ellen Silcock was born on the 16th December 1977 and was prescribed Wyeth's product Minulet in July 1993 when she was aged 15. On the 4th October 1995 when just under 18 she suffered a PE. She had similar symptoms. She is anxious and has sleep disturbance. She lost her job and cannot play sports.
Oral contraceptives began to be prescribed for women in the United Kingdom in the early 1960s. "The Pill" as it came commonly, almost affectionately, to be called rapidly achieved a significant share of the contraceptive market. Few if any pharmaceutical products have made such an impact on the lives of the persons for whom they were prescribed and the society in which they lived. It is no part of this judgment's task to analyse let alone evaluate the impact of the Pill on modern life. This much, however, has to be observed from the outset. As a pharmaceutical product it is almost unique in being prescribed for and taken by women who are, by and large, healthy and who choose to take it for the purpose of regulating their own fertility. There exist alternatives to oral contraception. Almost from the outset it was recognised as carrying risks accompanying the benefits it brought to those who took it. There has been a more or less continuous debate for 40 years in medical circles as to the nature and degree of those risks.
On the 18th October 1995 the CSM circulated a warning to all prescribers of COCs. This was a key event in the history of oral contraception in this country. The letter was addressed to doctors and pharmacists and was headed "Combined Oral Contraceptives and Thromboembolism". In its relevant parts it read as follows:-
"The Committee on Safety of Medicines has recently become aware of the results of three (as yet unpublished) epidemiological studies on the safety of oral contraceptives in relation to [VTE] The three new studies all indicate that combined oral contraceptives containing [DSG] and [GSD] are associated with around a twofold increase in the risk of [VTE], compared with those containing other progestogens in the light of this new evidence and in consultation with experts in family planning the Committee advises the following:-
(1) The recent evidence does not suggest any new additional risks with oral contraceptives containing levonorgestrel norethisterone or ethynodiol. Women taking these oral contraceptives should be reassured that there is no need for them to change their pill.
(2) Women taking oral contraceptives that include [DSG] or [GSD] should be strongly urged to complete their current cycle. The risks associated with unwanted pregnancies are far greater than the risks of continuing these pills.
(3) [COCs] containing [GSD] or [DSG] should not be used by women with risk factors for [VTE] including obesity, varicose veins or a previous history of thrombosis from any cause.
(4) [COCs] containing [GSD] or [DSG] should only be used by women who are:
- Intolerant of other [COCs] , and
- Prepared to accept an increased risk of thromboembolism"
The chairman of the Committee concluded with these words:
"I thought that it was important that you should be made aware of this matter at the earliest opportunity. However I am acutely aware that this new information will worry women and impose a substantial burden on doctors and pharmacists".
"since the re-analyses and new studies did not provide convincing evidence that the differences found . could be explained fully by bias or confounding".
It pointed out that the risk was small and that so long as prescribers and patients had access to full and understandable information there was no justification for restricting COC3s to those intolerant of COC2s, i.e. so-called "second line" prescription only. This is the UK regulatory authorities' final position as of today.
The following issues have been identified as those requiring decision in the case, and in the order in which I set them out.
(1) Have the Claimants proved that COC3s, alternatively DSG/GSD, carry a true excess risk of VTE which is more than twice that carried by COC2s containing LNG? There is agreement that this is the essence of the issue, though the parties do not agree how the drugs at issue should be categorised for this purpose. But all agree that if the Claimants fail to prove this the action should go no further as it could not succeed.
(2) If Yes, are the relevant products defective within the meaning of section 3 of the Consumer Protection Act 1987, i.e. was their safety "not such as persons generally [were] entitled to expect", which includes consideration of any instructions or warnings associated with the product? It is agreed that if the Claimants succeed on the first issue they must also succeed on the second. Realistically the Defendants accept that if the true risk of VTE was more than doubled, even if the overall risk was very low in absolute terms, women and their prescribers were entitled to be told of this before making their decisions or giving advice, and they were not.
(3) If Yes, have the Defendants proved, the onus being on them to do so, that they are entitled to the benefit of the Development Risks Defence under section 4 of the same Act? This applies where the:"state of scientific and technical knowledge at the relevant time was not such that a producer of products might be expected to have discovered the defect".
This will turn to a great extent on the true extent and limits of that defence, and the key question of whether it is restricted to what was capable of being discovered about the defect according to the state of technical knowledge prevailing at the time, or does it extend to what the Defendants might reasonably have discovered.
(4) If No, would the Claimants have been prescribed COC3s but for the defect? This issue includes consideration of the potential benefits in respect of matters other than VTE which they either brought or were perceived by prescribers to bring, relating to such questions as reduced androgenicity and better arterial cardiovascular protection.
(5) If Yes, in the case of each Claimant viewed separately , did her exposure to a COC3 cause or contribute to the adverse event which she suffered and but for the defect would she have avoided the injury of which she now complains?
SECTION B: THE APPROACH TO DECIDING THE FIRST ISSUE
As the evidence relied on by the Claimants and Defendants in this first issue in the case is almost entirely epidemiological in its nature it is necessary before going to the studies to state in simple terms the principles of epidemiology which apply.
In these a group of people is studied over a period of time. The experience of the members of the group who have the relevant exposure (here taking a COC3) is compared with that of those without such exposure and the incidence of the condition in question (here VTE) of the two groups is compared. Based on the proportion in which the two groups suffer the condition in question the relative risk (RR) of the one group against the other can be calculated. These studies are often the method of choice for observational epidemiological studies. They are however not well-suited to studies of the incidence of an outcome which is itself a rare condition since it will be necessary to recruit very large numbers of subjects in order to acquire a sufficient number of events to achieve statistical significance. They can also take a long time.
These studies are commonly used where the outcome under scrutiny is rare. The epidemiologist finds a number of "cases" who are people who have suffered the condition under examination. At the same time he recruits a larger number of "controls" who have not. These will usually be up to three or four times as many as the cases. Relevant data is then obtained about the exposure of both groups together with other risk factors. A comparison is then done between the proportion of exposed and non-exposed persons in the cases and the same proportion in the controls. From that is calculated the odds ratio (OR). For the purposes of this case there is little distinction between an OR and a RR and the two are often used, as I will use them, interchangeably albeit inaccurately. A case-control study is not capable of determining the absolute risk of the event in question since the incidence of the event in the population cannot be derived from it. It is therefore not capable of yielding the relative risk, unlike the Cohort Study.
A database such as the General Practitioners Research Database (GPRD) in the United Kingdom, which will be encountered in more detail below, constitutes a very large source of medical information on a large number of patients. This can be used by epidemiologists who are spared the need to recruit participants in a field study, and they are thus quicker and less costly. They can make use of the database to look back on data already accrued over a long period of time. These data can then be used to perform what amounts to a retrospective cohort study yielding a calculated RR or a nested case-control study yielding a calculated OR.
I have heard from ten epidemiological experts in this case and they remain as they have been for the last several years, largely irreconcilable in their differences. Such were those differences that before trial I was persuaded, against my initial judgement, by all the very experienced counsel in this case that no purpose would be served by requiring them to meet to resolve or narrow the issues. Having heard and seen them I can now understand why that was. The debate between them has been unyielding, at times almost rancorous in tone, and with a few honourable exceptions with which I will deal as I go through the issues, devoid of willingness to countenance that there may be two sides to the question. So, science has failed to give women clear advice spoken with one voice. I cannot simply accept the Claimants' categorisation of the Defendants' witnesses as eccentric mercenaries isolated from the rest of scientific opinion on this issue. From the literature I have read there are others who seem to share their views.
" The court has to evaluate the witness and the soundness of his opinion. Most importantly this involves an examination of the reasons given for his opinions and the extent to which they are supported by the evidence. The judge also has to decide what weight to attach to a witness's opinion by examining the internal consistency and logic of his evidence; the care with which he has considered the subject and presented his evidence; his precision and accuracy of thought as demonstrated by his answers; how he responds to searching and informed cross-examination and in particular the extent to which a witness faces up to and accepts the logic of a proposition put in cross-examination or is prepared to concede points that are seen to be correct; the extent to which a witness has conceived an opinion and is reluctant to re-examine it in the light of later evidence, or demonstrates a flexibility of mind which may involve changing or modifying opinions previously held; whether or not a witness is biased or lacks independence . There is one further aspect of a witness's evidence that is often important; that is his demeanour in the witness box. As in most cases where the court is evaluating expert evidence, I have placed less weight on this factor in reaching my assessment. But it is not wholly unimportant; and particularly in those instances where criticisms have been made of a witness on the grounds of bias or lack of independence, which in my view are not justified, the witness's demeanour has been a factor that I have taken into account"
That there is an advantage to be gained from the judge's impression of the expert witness notwithstanding that the issues may be technical in nature was stressed by Lord Bridge in Wilsher v Essex AHA  1 AC 1074 at 1091G.
The studies at the heart of this case have all calculated a point estimate, usually expressed to one decimal place. Almost invariably that is followed in brackets by two other numbers which constitute the lower and upper confidence interval. These are in all relevant places calculated within 95% confidence limits. Wherever in this judgment I follow a point estimate with two bracketed figures they will be the upper and lower limits of a 95% CI. A question is raised as to the relevance of these limits to the task I have to carry out. The Defendants say that to establish causation in the individual, and therefore a RR which is greater than 2, there must be seen not just a point estimate but also a lower CI which is greater than 2 in order for the result to be significantly different from 2.
(1) Walker in his report described the WHO All Centres figure 2.7 (1.6-4.6) and the TNS1 figure 1.5 (1.1-2.1) as "closely corroborative" of each other.
(2) Dr. Hershel Jick was taken to 2 RR estimates in his 1995 study report namely 2.7(1.2-6.3) and 2.0(0.9-4.8). His reaction was "these 2 estimates are not anywhere near statistically significantly different from each other. It is a flip of the coin sort of thing. One happened to be 2.7, one happened to be 2."
(3) Dr. Nicholas Dunn was taken to a range of ORs in a report which he had carried out, which will be encountered in the section on bias, which ran from 0.7 to 0.9 as against those in a parallel paper by Professor Lothar Heinemann which ran from 1.4 to 1.6. Because of overlapping confidence intervals he described these as not statistically significantly different and said it would not even be appropriate to describe these different examinations of the same phenomenon as pointing in different directions.
"We merely have to decide whether, on the material presented to him, as interpreted by the witnesses, the judge was entitled to conclude as he did, namely that on the balance of probabilities the cause or a significant cause of this Claimant's SCC was his wrongful exposure to large amounts of wood dust over many years. That does not mean that we are entitled to ignore known limitations on the value of statistical material or anything of that sort, but what it does mean is that we do not have to search for medical certainty, and even if we do uphold the judge's decision we can contemplate with equanimity the possibility that at some time in the future it may be shown, on a balance of probabilities or perhaps to an even higher standard, that the judge was wrong".
The lead claims in this litigation involve different brands of COC. The pleaded cases assert that each of these products is defective by virtue of it being not at least as safe as COC2s and conferring an increased risk of VTE in comparison with them. Because of the way the case is put in the pleadings and the Defendants belief in the heterogeneity of their respective products the two principal progestogens have in effect been separately represented throughout this trial.
SECTION C: THE WORLD HEALTH ORGANISATION STUDY
|All Centres||DSG||2.4 (1.3-4.6)|
|All Centres excluding Oxford||DSG||4.8 (0.5-43.4)|
|Oxford hospital controls||DSG||2.3 (1.1-4.9)|
|Oxford GP controls||DSG||1.8 (0.7-4.8)|
Was it an "a priori hypothesis" of the WHO Study to make a "head to head" comparison between COC3 and COC2 risks in relation to VTE?
"although not pre-specified in the study protocol, the secondary objective was to determine whether the risk of VTE .. varied with OC composition or duration of use." (And later) "these observations are based on an analysis of a secondary study objective, and the possibility that they are due to chance, confounding or bias or a combination of these cannot be excluded entirely. They must be confirmed by independent epidemiological studies .".
The Claimants' case here is that the all centres figure of 2.7 is the appropriate point estimate which should represent the findings of the WHO Study. Alternatively they say I should take a figure somewhere between 2.2 and 2.7. The Defendants say that the all centres data should be effectively discarded. I have already described the sparsity of the non-Oxford data as set out at Table 1 of the study. As will be seen from the table above, when analysed apart from the Oxford data the other centres gave ORs surrounded by very wide CIs indeed which would never be capable of standing independently as reliable evidence. The text of the WHO Study gives no direct assistance as to which figures it thought were the best estimate of the relative risk in this case. In the summary at the head of the paper the authors cite both all centres and Oxford figures.
The study authors expressed a clear view on this issue. They said hospital controls were the preferred comparison. While they accepted that "where there is homogeneous coverage of health services" GP-based controls may be more representative, their use in this study gave a markedly lower RR particularly for GSD which fell after adjustment to 0.9. They pointed to the high non-response rate among women approached as potential GP-based controls particularly in the younger aged groups. They said that the 18 orphaned controls for whom no GP-based controls could be identified were atypical and their exclusion "attenuated the higher risk associated with GSD compared with LNG". They gave no details of the numbers underlying these findings.
"when the authors examined cases for whom both hospital and community based controls were available they found similar RRs associated with the use of COCs containing DSG or GSD, regardless of which control group was used in the analysis."
"whilst ideally the aim of the control group is to provide an estimate of [COC] usage among women aged 20-44 who come from the same population as the cases but who do not have or have not had any of the three diseases under investigation, previous studies have met with major logistical problems in recruiting community based controls. Hence in order that a standardised method of control recruitment can be used in all centres, hospital based controls are to be used".
I do not see my choice as limited to the three main point estimates, 2.7, 2.2 or 1.4 in deciding what the best assessment of the WHO data is. Lord Brennan QC pragmatically invites me, if I have misgivings about the all centres figure, to fix on a value between 2.2 and 2.7. The Defendants say I should discount the 2.2 figure by a small amount to reflect the force of the argument in favour of the GP controls.
SECTION D: THE TRANSNATIONAL STUDY (TNS) - THE FIRST TWO STUDIES.
In October 1990 Professor Walter Spitzer of McGill University Canada was approached by the First Defendant's German parent company in the wake of the controversy following the findings of Professor Kuhl of Frankfurt. Kuhl had sought to demonstrate significant differences in the plasma levels of EE in women who took GSD as compared with those who took DSG and this had attracted much publicity and concern in Germany. Spitzer agreed to be Schering's consultant and advisor and set about structuring the response to this problem. He took steps to secure academic integrity by appointing a distinguished working group of international epidemiologists, doctors and biostatistician and a Scientific Reference Board (SRB) to supervise all scientific activities. Its members were not to be accountable either to McGill or Schering. He liaised with the German Regulator, the BGA.
Field work began in late 1991, but unfortunately Spitzer the principal investigator suffered serious ill health through much of 1992 which introduced some delay in the execution of the study. It had been agreed that the protocol would be published in a peer-reviewed Journal to permit scrutiny of it prior to the commencement of the study. That eventually was done and the protocol appeared under the names of Spitzer, Thorogood and Heinemann in January 1993(5). A time consuming part of such a study is the recruitment of cases and controls and this proceeded through 1993 and 1994. It became apparent that the initial aim of completing the study by the end of 1995 would not be met and therefore 2 further countries were added to the study in mid 1994, the name of the study being changed from Trinational to Transnational.
This was written in November 1995 by Spitzer, Lewis, Heinemann, Thorogood and MacRae, all of whom are witnesses in this action. It was published in the January 1996 issue of the BMJ, having been accepted for publication on 13th December 1995 (7). By this stage 471 cases of VTE were included and 1,772 controls matched for age within 5 year age bands and by hospital or community setting (789 and 983 respectively). The relevant findings were the UK and German data only, on the basis that the other 3 countries' data was considered fragile; Lewis said that these three, the so-called southern rim countries, was at this stage "in what one could call a run in or pilot status and were not yet in a position to deliver adequate data". Though as something of a political gesture a figure was given for the results from all 5 countries the entire focus of this paper, rightly in my judgement, was on the UK and German data, which I find gave the only meaningful information from which conclusions of any sort could be drawn. After this paper the southern rim countries disappear entirely from later deliberations by the TNS. Late in the case the Claimants accepted the force of this, and there is therefore really no issue about TNS 1, which stands on any view as a very powerful and influential study into this problem. It will be seen that it was based on 127 cases of VTE and 249 controls, compared with the WHO which had 71 cases, 48 of which came from Oxford.
|Comparison||COC3 v COC2||GSD v COC2||DSG v COC2|
||1.5 (1.0-2.2)||1.4 (0.9-2.3)||1.6 (1.0-2.5)
|OR||1.8 (1.0-3.3)||2.6 (1.0-7.2)||1.5 (0.8-3.1)
||1.5 (1.1-2.1)||1.5 (1.0-2.2)||1.5 (1.1-2.2)|
The lead author of this paper was Lewis and it was submitted for publication on 8th March of 1996 (8). Cases of VTE had now grown to 505 (though no new cases were recruited after October 1995, additional cases accrued from those already in the pipeline at that date), and controls increased to 1,877. This sought to complete the analysis of the TNS project at least in relation to VTE. It found ORs for VTE for all COC3s as against COC2s of 1.5 ( 1.1-2.0), or 1.6 (1.2-2.2) when NRG was included as a COC3. The figures for GSD as against COC2s were 1.7 (1.1-2.6), for DSG 1.8 (1.2-2.6) and NRG 1.9 (1.0-3.6). The authors called these "very weak associations" and therefore looked at issues of bias which might explain them. Specifically they looked at diagnostic and referral bias as well as a concept which they called the "attrition of susceptibles". The authors pointed to the fact that for women in the 25-44 year age band the year of COC brand introduction seemed to be of great importance, with the higher ORs attaching to the brand most recently introduced. This phenomenon even showed something which, viewed intuitively, seemed inexplicable and which also cannot be explained by the agreed evidence of the haematologists: Mercilon containing DSG and 20 ΅g of EE, a brand introduced in 1992, exhibited a much higher OR as against LNG (2.8) than its stable-mate Marvelon, containing the same DSG but a 50% higher dose of EE (30΅g) and whose OR was 1.5. Furthermore NRG, introduced in 1986-92, and so in chronological terms a COC3, had an OR of 2.4 as against LNG, even though in chemical terms it was more properly to be classified as a COC2 as it metabolised to LNG.
(1) The 12% reduction in the point estimate in TNS 1 when a fuller duration of use element was introduced into the model;
(2) The distribution of duration of use by age and product for the controls showed that among those who had used LNG in the 25-44 age group 20% had done so for more than 96 months as against younger women where the figure was 2%. With GSD no such effect was evident.
(3) Stratifying the data by dividing the study subjects into women aged 25 44 and 16 24 he found in the former group but not the latter a clear trend of increasing ORs related to recency of product introduction, the highest attaching to the most recent so that Mercilon with only 20 ΅g of EE showed the highest OR. This phenomenon is not explicable in haematological terms, according to the agreed evidence in that discipline.
(4) In a review paper in the Journal of Human Reproduction he published a finding from these data that the RR COC3 v. COC2 for 16 24 year olds was 1.36 (0.82-2.26) but for 25 34 it was 1.19 (0.74-1.98) and for 35-44 3.22 (1.47-7.06)
Organon launched its COC3 Marvelon in 1982; it contained DSG with 30΅g EE. In 1989 it launched Mercilon whose composition was identical except that the EE component was a third lower, 20΅g. In several studies Mercilon has paradoxically emerged with an higher OR for VTE. This is counter-intuitive in the sense that the received wisdom has for some time been that the risk of VTE is correlated with the dose of EE.
"that one should consider the interactions of the [DSG] with the [EE] which was the point brought forward by the Rosendaal article".
In fact when one looks at that Rosendaal article no such interactions are described as affording an explanation for the phenomenon. Rosendaal made the point that it was questionable whether the safety gains achieved in reducing EE progressively from 100-150΅g EE down to 50 or less could be continued by reductions from 50΅g down to 30΅g or 20΅g. In no sense did the article address the Mercilon phenomenon as Walker was obliged to concede. I was left with the impression that he had been rather selective in the parts of his original article that he chose to bring forward for presentation in this case.
When first articulated in TNS1 the theory of the "attrition of susceptible subjects" was put this way. It was said to be something which occurred:-
" ..because those patients susceptible to side effects tend to drop out of the corresponding user group at an early stage or are switched by their doctor to another product. In contrast if a product is well tolerated prudent doctors and safety conscious patients tend to continue to use it. So that patients who will have been taking a product for a long time would be expected to be at lower risk than first time users of any brand"
In TNS2, after noting the recency of introduction phenomenon the authors said:-
"the underlying phenomenon here is "attrition of susceptibles" or what may be termed a healthy user effect".
They supposed that such a group developed over time and that on the introduction of a new product the healthy cohort would ignore it and the newly introduced drug would be preferentially used by new users or those who did not tolerate the predecessor drug well. Therefore, the argument runs, there is a discernible population effect with short duration of use of COCs associated with higher risk and the depletion of susceptible users from the ranks of longer duration users. This has been caused by a differential introduction into the market of products rather than any inherent difference in effect of the generations of product and the apparently elevated RR visible in the 1995 studies is due to this.
(1) A withdrawal of susceptible women from the pool of LNG users as a result of VTE events. He argued that the incidence of VTE is too rare for this to cause sufficient attrition to account for the difference. Shapiro having reconsidered the matter agreed with this criticism.
(2) More women at high VTE risk might have withdrawn from the LNG user pool compared with COC3 users. For that process to cause a twofold difference, he argued, those who withdrew must have been a large proportion of high risk users at a substantially higher VTE risk than those who continued. Shapiro agreed with this proposition but said " we are talking about categories. Some have withdrawn."
(3) Thirdly, Farley dealt with the hypothesis that high risk women could switch from LNG to COC3s thus artificially enriching the latter group with more susceptible users. Against this he said that there had been no reports indicating a high relative risk in recent switchers. As to this Shapiro thought that it was common sense to say that high risk women would switch from LNG to COC3s if their doctors believed that the most recent product was the safest. He did not think that any of these factors operated independently but in combination. The Claimants say there is an insufficiency of evidence supporting a switching effect . Shapiro it has to be said was not impressed by Heinemann's "factor X" as a cause of switching (or for that matter, of anything else).
"we need evidence to support it. I think the evidence could come from a really straightforward and simple analysis of the TNS study without having to resort to all sorts of Cox regression or splines or particular kinds of sub-set analysis as were done .".
It is right to say that Lewis was asked whether he had attempted such types of analyses and he said he had, by performing several different types of stratification of the data. He was taken to task for not retaining or producing the results of this work, and I am invited to assume that his results were concealed as being unhelpful to the Defendants' case. I am conscious that Lewis has a direct commercial interest in obtaining work from these Defendants and to that extent producing results that are pleasing to them. All researchers in these fields are as Shapiro said under all sorts of pressures from industry funders, from their academic institutions and from publishers. I do not believe Lewis would go so far as to suppress unhelpful material. In TNS1 itself he had disclosed in plain terms that additional stratified analyses had been done. It has been open to the Claimants through their experts since February to run the type of further analysis McPherson was envisaging to refute this part of the Defendants' case.
Professor Samy Suissa in 1997 described an analysis he had carried out on a sub-set of the TNS data (12). He looked at 105 cases and 422 controls who were first time users of COC2s and COC3s or never users of OCs. This sub-set was a little under a quarter of the whole dataset. By applying logistic regression and quadratic spline modelling he found that for first time users the adjusted rate ratio of VTE as a function of the duration of OC use was:
"essentially identical for second and third generation pills relative to never users. This rate ratio increases to around ten in the first year of use and decreases to around two after two years of use remaining at this risk level thereafter for both second and third generations agents".
The use of quadratic spline models on epidemiological data was both novel and controversial. The spline is a "best fit curve", usually deployed in economics, as a complex method of fitting a smooth curve to data as they evolve over time, in which the curvature is allowed to change at different points of the analysis which are called knots. Therefore the conclusion which Suissa stated in his paper derives from the appearance of these curves, which for each of the two generations followed a more or less identical shape or course.
SECTION E: TNS 3 AND THE COX REGRESSION ANALYSIS
For all the cases and controls in the TNS study Lewis had available a month by month history of OC use from the age of 9 (the earliest date at which any study subject was prescribed an OC). If this was reliable and reasonably accurate it was something of a mine of information about the infinitely variable patterns of pill use and non use these women had followed. The calendars were described in the protocol for the TNS, which itself followed the WHO protocol closely, to this extent. Appendix I outlined the content of Form B which the protocol stated "will be used for the main interview of cases and controls". That content included:
"Contraceptive history in the 10 weeks before illness leading to current hospitalisation [or date of interview in the case of a community control] (the same questions also asked about lifetime use). This will include use of . Name or type of contraceptive".
The Claimants argue that this is thin support for the argument that it was an advance intention of the TNS study to use this calendar in the way it was in fact used.
Walker's criticisms are these:
(1) Its application has meant that women who are destined to become future cases are included in the comparison group or "risk set" for preceding cases. Because of the relatively low numbers of subjects in a case-control study the "future cases" as they might be termed will feature proportionately much more prominently in the study than they do in the general population. To the extent therefore that COC3 use is a predictor of future case status it will be over-represented in the comparator pool as against the general population and will serve to depress the relative risk.
(2) The TNS team made a specification error in the form of a faulty definition of co-variates by attaching the current exposure at the time of the VTE event (for a case) or index date (for a control) to all the earlier time periods for each study subject.
(3) In addition to this , in circumstances where, as he understood it, penetration of the COC market by COC3s was growing, and could be expected to continue to grow after the earlier case suffered her event, the result was that what was called the "current exposure variable" would become systematically enriched by increasing numbers of COC3 users among the controls in the risk set, or by the addition of what amounted to bogus exposed controls, which would have the effect of depressing the relative risk estimate. This last criticism, which was not central to Walker's thesis, does not survive the evidence of Dr. Hans Rekers which shows that the market shares of second and third generation pills were more or less stable from 1993-1995.
The use of Cox had been MacRae's idea, and it was reasonable for him to undertake the burden of seeking to justify it, he being a professional biostatistician. Lewis later deferred to MacRae, despite the fact that his own report carried over 10 pages of detailed treatment of the subject and I therefore had to consider whether he as lead author of TNS 3 was seeking to avoid questions he ought to have answered. He was a cautious and conservative witness and was not a statistician; I believe it was for such reasons that he took the course he took. It was also consistent with my trial philosophy, which was so far as possible to have one expert per topic where there were discrete issues such as this.
"the variable which will take on various values over time as the persons starts, stops, switches and so on different pills",
in other words it was in the jargon a "time-dependent covariate", indeed the only such variable.
".. an interesting application of a proportional hazards representation to a retrospective study . This is an unusual analysis but I can see no theoretical objection whatever to it; in a sense it is like applying a lot of logistic regressions to such data [ he referred to the Prentice paper] .It seems your analysis provides one convincing explanation for what is going on".
Sir David had allowed that opinion to go before the MCA appeal hearing in November 1998. He had not specifically been asked (and should have been, in my view) whether it could be used in this case, and had declined an invitation to attend as a witness.
The next evidence given, before cross-examination of MacRae, was by Walker who returned to the witness box to be re-examined. He re-asserted his view that the function of the Cox model was to look at serial cross sectional data, the cross sections being identified at the time of case occurrence, and to examine exposures which are defined as of those moments. The "risk set" in a Cox analysis he thought consisted of all individuals at risk of becoming a case on the date that the case actually became a case. Survival time was used "for indexing the comparison" as he put it but was not itself what was being predicted. To make good his point he then proceeded from the witness box to produce four pages of detailed algebraic calculations based on a formula which he had found in Lewis' report as Figure 5.10. Lewis had cited this formula, an algebraic expression of the maximum likelihood function, to show the similarities and the differences between Cox and ordinary logistic regression.
MacRae maintained his view as to what were the "risk sets" or exposure groups namely the individuals in the different strata or sub-sets of the co-variates specified in the model whether fixed (e.g. BMI ) or time-dependent (e.g. prior OC use). He said that Walker's exercise, which he had evidently carried out very shortly before going into the witness box on Day 14, was flawed. He believed that Walker had failed to disable "ocgennw" at least in its most important part, that is to say more recent exposures. The Defendants submit that it is plain that Walker's exercise left into account the most recent pill history for study subjects namely that pertaining to the years 1993, 1994 and 1995. It was therefore, they argue, not surprising that the 0.84 figure Walker had derived was not dissimilar to the TNS Cox figure of 0.79. MacRae's evidence was that the matter was best tested by disabling "ocgennw" completely. He said he had done so on the previous evening and the resultant hazard ratio went up to "nearly 1.2". Though he offered to produce those logs he was not taken up on that during his evidence.
Separate from the passage in his evidence I have referred to above Walker in the Appendix to his third report calculated algebraically that it would have been necessary for COC2 users to have used OCs for about 6 ½ years longer than typical periods of use of COC3s to produce the effect shown by Cox, which was both implausible and unsupported by any observation reported. He had based this calculation on Lewis' Appendix XIV from which he took the apparent effect of the "curd" variable of 0.992. The Defendants answer this by saying that this figure comes from a calculation in which "ocgennw" has already done its work and achieved the main adjustment for past history. Therefore the premise on which this argument is based, a supposed decline in risk of 0.992 per month or 9.2% per annum is a false one. I believe the Defendants' answer to this point to be right.
In my judgement the key calculation is that culminating at 7.54 of the Claimants' Black STATA File in which MacRae unequivocally removed any form of adjustment for past history and obtained a Hazard Ratio which increased in the manner he would have expected it to.
(1) Walker was not familiar with this model. He did not, for example, really know what the instruction "stset", fundamental to the survival time analysis, meant. He misunderstood the respective roles and inter-relationship of "cgennw" and "ocgennw". He thought that the "curd" and "d" variables controlled all past history. To a great extent this was compounded by the late date at which he was able to get access to the data, through no fault of his I should stress.
(2) His first report attacked Cox in a superficial and misdirected way. He did not say, as he should have, that he needed to see the data before commenting. It contained no hint of what were later to become his views. His re-examination evidence was in both its main areas a new line of attack, both evidently having occurred to him shortly before his return to the witness box. His difficulties were understandable, but it was always open to him to decline the role of Claimants' protagonist in this complex area of the case.
(3) MacRae in his reports and oral evidence gave a clear and confident account of the model's operation, its use having been his idea. He was an experienced biostatistician, whose generic evidence on statistics was barely challenged. He had used Cox many times before, though never in such a case as this. He cited, in my view correctly, and as Walker had not, the Prentice & Breslow paper (16) as authority for the theoretical appropriateness of its use in a case-control study. He impressed me as having a good command of the subject.
(4) MacRae's calculation culminating at page 7.54 when he removed "ocgennw" entirely seems a highly persuasive demonstration that the model worked in the way he said it did and that he had not introduced any specification error into its operation.
(5) The unique nature of the exercise meant it had to be approached with circumspection, and I confess to some scepticism when I first read about it. But I accept that the lengthy longitudinal data of good quality made this study entirely appropriate for the deployment of this model. No equivalent allowance for past use and its effects could be achieved by stratification or other methods of regression, since the complexities of 2,300 odd detailed histories with 17,500 odd discrete episodes of use would have been such as to make such a course impossible. If there had been no effect from duration of use I am satisfied no violence would have been done to the original TNS figures by the use of Cox.
(6) Cross-sectional risk-sets as envisaged by Walker's Slide 26 error would have been entirely inconsistent with the essential concept underlying Cox (in Chapter 1 of his 1984 book) of survival time to failure, namely a longitudinal consideration of the data.
(7) If enrichment was a problem, as it would indeed have been if Walker was right, the whole virtue of cross-sectional studies being that they enrich the dataset with cases as compared with follow up studies, then its tendency to bias the results to the null should be apparent in COC1s, and there was no such effect either in MacRae's or Walker's further work on Cox.
(8) Sir David Cox would I am sure have paid attention to the use of his model in such a controversial area and is likely to have noticed if its use was inappropriate in any way; I must not place too high a value on this as he did not give evidence before me, but I cannot close my eyes to his views.
(9) As to the problem of "time", since the "risk sets" or exposure groups were followed to failure on a survival time basis MacRae was right to say that whether the time axis was calendar or age was a "distinction without a difference" since the function of the axis was to measure the risk or time to failure, not to organise the "risk sets".
(10) Past use of COC1s appeared from the calculations to be associated with a reduced risk; this would be expected where women who had survived a period of COC1 use changed to less thrombogenic pills.
SECTION F: THE JICK V FARMER DEBATE
In about 1988 a commercial company named Value Added Medical Products Limited (VAMP) which had supplied computer systems to general practitioners for some years set up a research databank based on those systems. The idea was that those doctors participating would receive financial incentives to do so. They in turn agreed to follow a protocol for the recording of clinical data relating to their patients and to transfer those data suitably anonymised to VAMP on a periodic basis. VAMP would then commercially exploit this database by licensing research bodies to use it.
Jick, prior to 1995, had had no involvement in any scientific consideration of COC3s, indeed he had never heard of the names of the products concerned, although his group had done a number of studies in the 1970s and 80s on VTE and COCs generally. He approached the matter entirely afresh, as I accept. In 1995 he carried out 2 studies. The first which has been called his mortality study was in response to a message from the ONS about young women who had died while taking a COC containing GSD. The findings of that study, while interesting, do not bear on the issues in this case. The second study which was to be a morbidity study, and which I will call Jick 1995, came in response to an approach at about the end of June or possibly the beginning of July when the so-called unexpected findings of the WHO were rising to the surface. Someone "fairly high up in the MCA" as he put it and another person who worked for Organon had got wind of this pending announcement and asked him to use the GPRD to do a study on the topic. Both studies were eventually published in one paper in the same issue of the Lancet on 16th December 1995 (19) as that which contained the two WHO studies and one from the "Leiden Group" in Holland, with which I will deal later.
"Age, practice and calendar time were closely controlled by matching. While both smoking and BMI were independently associated with an increased risk of VTE, controlling for them only slightly changed the RR estimates . confounding by age, practice, calendar time, smoking and BMI is thus unlikely to explain the associations found. The inclusion of only otherwise healthy women minimised the possibility of selection bias for OC prescribing. The high quality and completeness of the recorded clinical information had been previously demonstrated, and there is little reason to suspect that the results were due to a bias in recording either exposure or outcome. Nevertheless an observational study such as this one cannot rule out additional biases particularly selection bias, which may provide a noncausal explanation for the observed association".
This study had started sometime in July and was completed and sent prior to publication to the MCA some weeks before the Dear Doctor Letter of 18th October, that is to say within about 2 months or so of its start. It was the third unpublished study referred to in the dear doctor letter. The final conclusions of the authors are interesting. They said:-
"This study and the WHO one provide evidence that the risk of non-fatal VTE among recipients of the new generation OCs . may be about twice that for older OCs .... the new generation preparations may lower the risk of arterial thrombosis. In view of the modest increased risk for non-fatal VTE noted for new generation OC's in the available studies, and the absence of a substantial difference in risk for cardiovascular deaths in the current study, it may be premature to conclude that third generation OC's compared with older OC's confer an increased risk for cardiovascular illnesses as a group".
a) The periods covered by each study were different.
b) Jick based his figures on 75 cases (52 exposed to COC3s) drawn from 370 practices; Farmer used 296 cases (139/146 exposed to COC3s for year of birth/5 year controls) drawn from 618 practices.
c) Jick restricted his study to users of DSG, GSD or LNG. Farmer included women using any COC on the relevant date.
d) Jick excluded fatalities; Farmer included them.
e) Farmer considered women from 40 to 49; Jick excluded them.
f) Jick obtained case exposure data from hospital records and control exposure data from the database. Farmer obtained these data from the same source namely the database.
g) Farmer had 5 categories of BMI the highest being 35 plus; Jick had 3 the highest being 25.
h) Farmer adjusted for asthma; and Jick did not.
i) Farmer matched controls to cases by year of birth as well as 5 year banding; Jick used 5 year banding.
"in our study the ORs for individual products did not differ significantly when cases were compared with the exact year of birth match controls. On the basis of the current analysis we do not believe there are differences in risk between COCs"
|STUDY (and controls)||PRODUCT||COC3 CASES (n)||RR (Adjusted)|
|Jick 1995 ( 5 year)||DSG||30||2.2 (1.1-4.4)|
|Farmer 2000 (year of birth)||DSG + EE 30||62||1.0 (0.6-1.6)|
|(5 year)||DSG + EE 30||65||1.4 (0.9-2.1)|
|(See Jick V p.3)||ALL COC3s||140||1.2 (0.9-1.7)|
|Jick 2000 (year of age)|
|Pre-scare period||COC3||54||2.2 (1.1-4.3)|
|Post-scare period||COC3||10||2.8 (1.1-7.3)|
|Both periods||COC3||64||2.3 (1.3-3.9)|
|Jick 1995 + 2000 (mixed)||COC3||104||2.2 (1.5-2.3)|
|Cases in Common|
|With Jick controls||COC3||68||1.8 (1.1-2.9)|
|With Farmer controls||COC3||68||1.3 (0.7-2.2)|
Notes: 1. All comparisons are with LNG.
2. None of Farmer's results is statistically significant.
3. All of Jick's are, bar 1995 GSD.
4. All the results are statistically compatible in that their C.I.s overlap.
5. For cases in common, see later.
In his first report dated 26th July 2001 having described his own studies Jick dealt with Farmer's criticisms, as he then understood them to be (the two had met, corresponded and disagreed before the start of this litigation). He described Farmer's comments on the width of his age matching as naive and a product of his inexperience in pharmacoepidemiology. So far as Farmer's studies were concerned his criticisms were these. He said that Farmer had used "hundreds of practices that the BCDSP has found to be of unsatisfactory quality and completeness", that he used 10 OCs' exposures in his matched analysis rather than COC3s against LNG "which were the only preparations evaluated in our published study"; that the numbers provided in at least one of the critical tables in the Farmer study were incorrect; and that many non-idiopathic subjects were not excluded who should have been.
"gone through in considerable detail, because they cannot both be right, using the same database".
The Claimants' opening note contained a helpful tabular analysis of the issues in this area of the case which made no reference to controls at all. For his part Mr. Underhill opening the defence on this issue put in a 5 page note based on Farmer's work and said to have been approved by him (which contained an egregious error by Farmer which I will have to deal with later) but which concentrated entirely on the question of case inclusion and exclusion.
"significantly skewed towards third generation OC users . the effect of this is to significantly depress the RR".
This report though only some 15 pages long was extremely dense and included 15 detailed tables in which the controls used by Farmer were closely analysed and dissected. Thereafter Farmer responded to it with a series of notes and Jick himself provided a short addendum to his fifth report on 27th March 2002.
Two main issues emerged on the question of controls which came to dominate this debate. The first was age matching and the second the inclusion in Farmer's study design of COCs other than GSD and DSG.
|Original (Informative) Set||DSG||DSG||GSD||NRG||NRG|
(which is concordant, non-informative, and therefore ceases to contribute to the analysis)
(which is still discordant and therefore informative but is now reduced to a 2 control set from a full set).
Jick then proceeded in a series of tables to set out what he considered flowed from this procedure. He showed where there was a lower number of controls per set that LNG exposure was more prevalent than in full 4 control sets. Example 2 above shows a possible illustration of how this might happen. But Jick in evidence merely said there was:
"some kind of peculiar mechanism, bias, whatever you want to call it, which produces different results depending on the number of people in your set. I have to admit that that was a surprise to us because that does not normally happen."
When challenged in cross-examination to explain how it could be related to fine age matching he in effect declined to address the question.
The Claimants submit that this debate should be resolved by me in favour of Jick's studies and that Farmer's findings should be omitted entirely from my final considerations as being of no value at all. The Defendants contend that the Farmer study is preferable, because it was bigger and therefore better, but that in the alternative I should look at the area where there was agreement between the experts as to case selection and use those as being the basis for my evaluation of this group of studies based on the GPRD. The Claimants adopt Walker's criticism of this compromise approach as "cutting the baby in half". Before embarking on this stage of my judgement it is necessary and appropriate to set out my evaluation of the protagonists as experts and as witnesses.
"In observational studies it is important to take account of the fact that spurious associations may be found if there is a factor that is either associated with an exposure or the outcome or both. These are called confounding factors".
a) Jick used fewer practices (in Jick 95 he used 365 and in Jick 2000 288; Farmer 2000 used 618).
b) Jick's studies were based on fewer VTE cases (75 and 106 as against Farmer's 285) and fewer of those exposed to the study drugs; in Jick 95 when he divided COC3 into DSG and GSD his cases were 30 and 22 respectively when Farmer's were 83 and 63; in Jick 2000 when he aggregated the study drugs as COC3s he identified 64 cases whereas the same figure for Farmer 2000 would be 140 (per Jick V Table 2).
c) Both Jick studies were executed in some haste, Jick 2000 particularly so and for the reasons I have stated above; this was not the case with Farmer's work.
d) The basis on which Jick selected his sub-set of practices, as I find, was primarily to confine himself to those who were compliant with his requests for further information on study subjects. He accepted that was a reason which had "nothing to do with the quality of the data provided by that practice to the GPRD". Farmer used all practices accepted by the GPRD as up to standard. I do not accept Jick's evidence that the GPRD did not exercise proper surveillance of practices from that point of view.
e) There remains an unresolved dispute as to whether Jick was over exclusionary in his approach to the admission of cases and/or whether Farmer included incorrectly cases which were not true cases and/or which were not idiopathic cases of VTE.
f) Jick had no advisory group. Farmer's advisory group met 4 times and played an active role.
g) Jick had no preconceived ideas prior to Jick 95 and came fresh to the subject; conversely his motivation in Jick 2000 was to refute Farmer's case. Farmer's track record is much less satisfactory and, there is no doubt, he saw his academic future as largely consisting of executing studies for drug companies in this field.
h) Jick had space problems on his own computers; Dean said, reliably as I find, that he was always keen to "lose" practices to make space; to some extent Jick confirmed the problems that the size of these data could cause in his own evidence on Day 19.
i) The asymmetrical ascertainment of case and control exposure in Jick 1995 was described by Thorogood as "not the best design" and something which could have led to selection bias, though it should be said she remained a believer in the superiority of this study. Shapiro was also critical of this feature.
SECTION G: THE OTHER STUDIES
The editor of the Lancet procured a fourth paper for inclusion in his December 1995 edition to go with the two WHO papers and Jick 1995 (24). This came from the so called "Leiden Group" whose research into thrombophilia has been of the highest quality and is internationally recognised as such. The paper identified a RR for DSG as against LNG of 2.2 (0.9 5.4). There were no data in this study relating to GSD at all. The RR for DSG based on 37 cases and 15 controls was 8.7 (3.9 19.3) and for LNG based on 20 cases and 18 controls 3.8 (1.7 8.4). In purely statistical terms therefore the relative risk between DSG and LNG was not statistically significant and the confidence intervals involved were wide reflecting the low number of cases and, particularly, controls.
In a research letter in the Lancet in 1999 Herings and others published research based on an automated database in the Netherlands into women between the ages of 15 and 49 who used COCs between 1986 and 1995 (27). The study is not very fully described. There was no nested case-control study. As originally published it looked at what it described as new users of COC2 and COC3 products as between whom the text said there was an RR of 3.5 (1.4 8.8) although the table gave a crude figure of 3.7 (1.5 9.1) and an adjusted RR of 4.2 (1.7 10.2) the adjustment being for year and age. Thorogood and Shapiro both took the 3.5 point estimate as being the conclusion of this study. Walker and McPherson took 4.2. In a second letter to the same journal (28) they extended the study to what they called "recurrent users" of whom they had found 78 cases and for whom they gave a crude RR of 2.3 (1.5 3.7).
This was a New Zealand based case-control study of fatal pulmonary embolism in 36 women aged between 15 and 49 (29). The main purpose for which it was cited as being important by the Claimants' experts Walker, Thorogood and McPherson, albeit without great emphasis, was that being a study of fatalities it was one in which selection bias would not have been in operation. I agree that that was the case and that Shapiro's criticisms on this point are far-fetched and not well founded.
"The high mortality in New Zealand may partly reflect the extensive use of third-generation oral contraceptives, which seem to carry a higher risk of VTE than older contraceptives".
was not one which Thorogood would have included in the study had she been responsible for it and Shapiro agreed it was not justifiable. More sophisticated arguments were addressed on the likely effect of the loss or exclusion of controls but I am not greatly impressed by that line of attack. The Claimants put this study forward tentatively. Walker did not include it in either of his meta-analysis procedures. At best it seems to me it represents a study from another country from which can be deduced an elevated relative risk consistent with other studies. However the weight to be attached to it in statistical terms is in my judgement extremely small.
Lidegaard and others carried out two studies in Denmark in 1998 (30) and 2002 (31), the second of these being published during the course of the hearing. The first was a study of Danish women aged 15 to 45. Cases were identified from the Danish National Patient Register and controls were women interviewed in a study on the risk of stroke in relation to OC use and who had originally been matched by age to cases of stroke. The choice of controls, it is accepted by the Defendants, vitiates this first study and renders it of no value, albeit it appeared to find no significant evidence of an increase in risk for COC3 use as against COC2; after adjustment for duration of use the RR produced by the study was 1.44 (0.83 2.5). The controls used were of a different age profile, enrolled at different times and there was asymmetrical information concerning potential confounding factors all of which Shapiro in his written report rightly described as "unacceptable".
This study was Farmer's first foray into COC / VTE research. He was approached by Organon in early 1991 who commissioned a study at a cost to them of £88,000 based on the Meditel database. This was a privately owned software system which had been sold to certain general practices. The data were collected by the owner of the business and supplied in crude form to researchers. Of the projected price the cost of data was some £55,000, and most of the rest went on a computer programmer.
I will not lengthen this judgment by dealing with this at any length. The Defendants in their closing submissions lay no emphasis on it as likely to assist me. Farmer himself described it as "not pivotal" nor was it corroborative in his view but merely "in line with" other results he had found. I ignore it.
Farmer carried out two studies based on this database which, unlike Meditel, was a research standard source of data of this kind.
This is a curious study which was never published and exists in draft form only (35). It is huge, and runs for some 85 pages. It is signed at the end of 1997 by four employees of Wyeth-Ayerst, as American company associated with the Third Defendants. three other employees of the same company signed it as reviewing and/or approving it. Dean and Thorogood are both listed as consultants to the study, a status which both explicitly and strongly rejected in evidence.
This paper was an attempt by Farmer to test the CSM view of a doubled risk in a way that any non epidemiologist would regard as eminently sensible (36). It has received a critical reception which I do not think it entirely deserved. His thinking was that if COC3s did indeed carry a doubled risk, and when their use had declined from 53% to 14% almost overnight, then one should be able to see an effect. The CSM's intervention was after all designed to achieve an effect in public health terms. The presence or absence of that effect should be the best way to resolve the issue.
SECTION H: BIAS AND CONFOUNDING
"The possibility that they are due to chance, confounding, or bias or a combination of these cannot be excluded entirely".
Dunn was of the view that this occurs where a doctor might preferentially prescribe COC3s to those at an elevated risk of VTE. This might in my judgement happen because COC3s were or were perceived to be safer in thrombotic terms either because of the prescribers' understanding of the marketing thrust behind them, or because in a more loose way he/she thought that they were newer therefore they must be safer. In fact the claims made for COC3s, properly considered and construed, were that they offered increased safety in relation to arterial disease as opposed to problems on the venous circuit. The predictors for arterial disease (hyperlipidaemia, hypertension and smoking) are not, with the possible exception of the last, predictors for VTE. At all events in Dunn's view, and Walker agreed with him, at least where known risk factors for VTE drive the differential prescription this is not a true bias but rather a form of "confounding by indication", in the jargon term, and can be allowed for when the statistical analysis is adjusted for the various risk factors which drive it. Heinemann accepted this proposition in studies where the data gathered covered all risk factors, and I accept it too as it is plainly a logical proposition.
That leaves for consideration another distinct form of bias which could be called diagnostic or referral bias. Heinemann of course saw them as all part of a continuum. Referral bias if present is a true bias in everyone's view, and is in reality closely connected with prescriber bias and diagnostic bias. It must be considered against the background that it is common ground that VTE is not an easy condition to diagnose. Its initial symptoms, typically leg pain and swelling, can easily be mistaken for other conditions. It may also resolve spontaneously and leave no lasting sequelae. Throughout the studies one can sense an awareness of this problem.
Parkin (29) based on data from New Zealand, and already referred to in Section G paragraph 234 above. The point of the study was that its cases would be unlikely to be affected by diagnostic bias since "most young women who die unexpectedly are referred for necropsy". That said and acknowledged it is not of great use as establishing or refuting the existence and effect of this form of bias unless confidence can be reposed in its results, which I have already said I cannot do save to a very small extent.
There is little left of Heinemann's version of prescriber bias. In so far as they are distinct entities referral and diagnostic bias are plausible forms of bias in this case, but there is no clear evidence as opposed to suspicion that they were in operation in such a way as to affect the point estimates in an upward direction. If therefore the resolution of the first issue depended on whether some overall point estimate derived from the relevant studies which was over 2 should be reduced below 2 to account for the biases discussed above, while I find myself suspicious that these or some of them may one day prove to have been in play, I would not be able to say on the evidence before me that they probably were, or that it would be right on their account to reduce the values which I consider that the studies otherwise show before arriving at a "true" RR. That leaves only for consideration the possibility of hidden multiple biases.
It is widely accepted that observational epidemiology, especially where it is dealing with weak associations and non-infectious disease risk factors, is working at the limits of its operating range. This combined with the readiness of the scientific media to pick up and run with environmental health scare stories makes for a potentially dangerous mixture. But a thoughtful article in the American journal Science in 1995 (46), with whose fundamental message Walker was in substantial agreement, underlines this problem. The well known statistician Norman Breslow whose work has been encountered elsewhere in this case said in connection with advances in methodology in this area:-
"Today people are doing much more in the way of mathematical modelling of the results of their study, fitting of regression equations, regression analysis. But the question remains: What is the fundamental quality of the data and to what extent are there biases in the data, that cannot be controlled by statistical analysis? One of the dangers of having all these fancy mathematical techniques is people will think they have been able to control for things that are inherently not controllable".
The attainment of statistical significance does not answer this problem, since it eliminates the play of chance only. No less an authority than Sir Richard Doll of Oxford University is quoted in the same article as saying that no single study is persuasive by itself unless the lower limit of its CI falls above a threefold increase risk. Others have put this yardstick at a fourfold risk.
"This conclusion can be reached only after alternative explanations for the finding are excluded as implausible. These explanations include coincidence, bias and confounding. Observational studies can never fully eliminate the effects of bias and confounding . It is especially important to consider which of the numerous potential biases or sources of confounding are likely to have affected a particular study, and what effect these may have on any inferences from the study".
The Defendants do not pin their colours to any particular mast but say that there are here in operation a number of potential biases in addition to those specific forms of it with which I have dealt with above which have an additive affect. Where there is a weak association by definition it will be more sensitive to the effect of bias and lead therefore to a greater need to examine the possibility.
"In light of the above and, indeed, for any small or even moderate associations I suggest that the question is not whether we can devise some scenario that could produce the relative risks that we observed. Rather we should ask: 1. What evidence exists that upward biases are present and that they outweigh biases in the other (downward) direction? And
2. How does the evidence for such biases compare with the evidence for causality, i.e. is it more or less convincing?"
This seems to me a sensible approach to the question. Shapiro's own views on what was called "Heinemann's Factor X" are in point on this question, albeit given in the context of residual confounding by indication. He said:
" . there is a point where we are not permitted to speculate in that way, so it would not matter. May there be some factor X which is connected both to the exposure and to the outcome? My attitude is I suppose there might be, but I want something more than just a supposition to go on [on] this"
With this I agree.
I cannot, as already stated, identify the evidence which I feel I need to see in this case to allow me to say that prescriber, referral or diagnostic bias together or separately have been in operation in the main studies in this case in such a way as to account wholly or to some measurable extent for the elevated point estimates in them. Nor can I find that some residual innominate form of bias or confounding has so operated. The remaining candidate is a form of confounding factor or bias introduced by the so-called duration of use effect, where again suspicion or speculation however appealing is not an adequate basis for judgment in this case. Cox if right remains the only hard evidence for it, and if it is right as I believe it is it is both solid and compelling evidence for its existence and the direction and magnitude of its effect. But for Cox I would be obliged to find that the main study results stand at the values I have attributed to them, and that there is no warrant for further reducing them from the figures I have indicated above to arrive at a "true" as opposed to a merely apparent RR.
This section is perhaps the convenient place to deal with this form of bias, said by the Claimants to operate in the opposite direction. It does not relate to the data as such, but describes a state of mind present in those conducting studies supported financially by drug companies. The word is used in a way much closer to its everyday sense.
SECTION I : CAUSALITY
The famous epidemiologist Sir Austin Bradford Hill in an address in 1965 considered the difficult question of when a statistically apparent association between A and B should be translated into the proposition that A causes B (52). He proposed nine criteria for consideration, which have been described as an attempt to systematise common sense, but which repay consideration. I set them out in his (descending) order of importance.
(1) The strength of the association. He cited the 9-10 fold difference between smokers and non-smokers in terms of the risk of cancer and the 20-30 fold increase for heavy smokers, as against the two fold increase for coronary thrombosis. Here we have weak associations at best, which on their own are not strong support for a causal link.
(2) Consistency derived from repeated observations by different persons in different places and at different times; Cox apart there is considerable consistency here in my findings in the overview section which follows , albeit the studies are all retrospective and none is prospective.
(3) Is the association specific to the exposure in question? This is an example of a question capable of being blurred by aggregation of COC3s. If they are separated out into different progestogens specificity becomes less clear.
(4) Temporality; on any view the cart comes after the horse as it should.
(5) Biological gradient; the Mercilon phenomenon weakens the argument for causality, as would a heavier death rate in light smokers had such been found.
(6) Biological plausibility; I will deal with this under Haematology below. Bradford Hill accepted that this was a feature which could not be insisted on, since to do so would be to hold up the increase of knowledge until experimental science caught up with valid advances made by observational studies.
(7) Coherence is what is known of the relationship coherent with all other knowledge; the WHO gave the answer to this when they called their original finding "unexpected".
(8) Experimental evidence. None can be prayed in aid here, nor could there be any in this field.
(9) Analogy from other fields. No assistance comes from this.
Initially this issue was due to take three weeks of the court's time and involve five expert witnesses. In marked contrast with the epidemiologists, this area of the expert evidence was dealt with in a commendably sensible and cost-saving way. That it did so is due to the strenuous efforts of counsel and the open minded and professional way in which the haematological experts assisted the court. Counsel drafted before trial a comprehensive and clear set of questions to be addressed by the experts before trial, and the experts considered them and gave clear answers. The result was that the remaining issues were greatly narrowed and disposed of in one day rather than 15.
(1) Factor VII is raised on average by 19%. Professor Machin for the Claimants believed that this had a probable causal effect increasing the RR of COC3s, but the Defendants' expert Dr Baglin did not accept that there was any evidence of a causal relationship;
(2) Free Protein S was reduced by 15-17% and either "certainly" (Machin) or "possibly" (Baglin) associated with VTE;
(3) ETP as measured by the Rosing assay was "altered significantly" by COC3 use, though it was not possible to express this as a percentage.
(4) Thrombin activatable fibrinolysis inhibitor (TAFI) was increased by some 2 4 %. Machin thought this a possible contributory factor, Baglin an improbable one.
(1) The Defendants do not contend that a "true" RR of more than 2, which the Court may find proved on the basis of the totality of the epidemiological evidence, should be rejected on the basis that the evidence of a mechanism is absent or inadequate.
(2) The Claimants do not contend that, if the epidemiological evidence fails to establish such an RR, it should nevertheless be found proved because the haematological evidence establishes that there is a mechanism which accounts for such an RR.
(3) There is no biologically understood reason that would explain an epidemiological finding (if there is one) that 20 ΅g EE pills carry a higher RR of VTE than 30 ΅g pills with the same progestogen and this would not be expected to be the case on the basis of present haematological understanding.
(4) It is agreed that there is no distinction to be drawn between DSG and GSD as to their effect on the haemostatic factors of relevance to this case.
(5) The following is agreed in relation to the effect over time of COCs on haemostatic variables:-(i) the effect is produced essentially within one treatment cycle andcertainly by the third;(ii) there are no further changes with continuing COC use;(iii) during the pill-free week (if taken) there is a slight reduction in haemostatic effects. If the pill-free week is not taken there is no such reduction;(iv) on discontinuance, the haemostatic effects of COC use disappear within 6 weeks and largely after 2 weeks, i.e. levels of coagulation factors return to baseline, with no past user effect.
"theoretical(TB)/hypothetical(SJM) model . a simplistic approach to help understanding of a complex issue, but [which is] of no direct quantitative value for individual patient's risk estimates".
There has yet to be any haematological study on a long term follow-up basis over 20 years or so such as would be needed for a full answer to be given to this. The assistance I get from Rosendaal is slight. Haematology neither advances nor precludes a "duration of use" argument; this can only be resolved by epidemiological means.
SECTION J: OVERVIEW OF THE STUDIES
|TNS (S.RIM )||5.2||2||13.6||4||5||10|
|TNS (UK+ GER)||1.73||1.15||2.38||29||45||74|
|UK MEDIPLUS 97||1.34||0.74||2.39||11||15||26|
(1) It includes for the WHO study the all centres RR of 2.7, not the results for UK/Germany only; two of those linked to the study who gave evidence, namely Thorogood (on its writing committee) and Heinemann (an investigator) though the Oxford hospital based figure of 2.2 was the best estimate.
(2) It includes one GPRD study only, Jick 1995, and rejects Jick 2000 and Farmer 2000.
(3) It includes, albeit with a very low weighting, the Southern Rim data which most others discarded, and which the Claimants themselves also now exclude.
(4) It excludes TNS 3, the Cox regression analysis based on the pill calendar data.
(5) It includes Leiden 95, and gives it a maximum score for design weight, when serious criticisms have been made as to its reliability as a relative risk study.
(6) It excludes Lidegaard entirely, rather than including it with if appropriate a reduced design weight.
"roughly a doubling of risk at least double probably more at least 1.8 fold very likely to be in excess of 2 unequivocally in excess of [1.93] in excess of twofold the overall results from independent studies would indicate a relative risk of around [2.4] with confidence limits between [1.9 and 3.0]".
(1) In relation to Leiden 1995 he described the study as giving RR estimates for the third against all other OC types. In fact the study considered DSG only and not all third generation. Although in cross-examination he accepted that the "buddy" controls used by this study were "not the kind you normally expect to see" this did not appear in his report nor did any statement to the effect that the numbers involved were low.
(2) He described Farmer's Meditel Study as a study based on the GPRD for 1990 to 1991. This was no slip of the pen since he made the point (wrongly) that it therefore covered some of the same data as Jick 1995. He said the risks were calculated for second generation OCs when the comparison was with first generation. He criticised Farmer's failure in this report to analyse the risks associated with particular progestogens not withstanding the fact that this report was submitted for publication at the end of 1994 when such a debate had not yet started. He in effect accused Farmer of concealing data on the relevant risk of different progestogens and called his article "no more than polemic in the debate about the role of the particular progestogens". This was an unfair criticism in my judgement; in any event after the pill scare occurred Farmer did publish such material as he had in this category, but up to then it had not in my judgement been relevant information.
(3) In his criticism of Lidegaard 1998 he stated that it was "quite interesting" that notwithstanding what he called manipulations of data within the study "nowhere is a direct comparison with confidence limits made of third v second generation pill". In fact quite plainly there is exactly such a comparison evident on the face of the report.
(4) Dealing with Jick 2000 he described this as "clearly an excellent study .". In cross-examination he said he was not aware that Jick had not verified the cases in the same way that he had in Jick 1995 though that is again plainly there to be seen on the face of the study itself.
(5) He wrongly described the Farmer Pill Scare Paper as having used the GPRD for 1993 to 1995 instead of to 1998. This was more than a slip; the whole point of the paper was to compare the positions before and after the scare. He criticised it for not attempting to examine particular effects of any pill type without apparently appreciating that that was not the purpose of the study; that attempt was made in Farmer 2000.
(6) In the Farmer Validation Paper he misread the summary stating that it used 286 cases plus 177 additional events; plainly the 177 were a sub-group of the 286.
(7) In his commentary on Suissa 1997 he states "data were presented for third generation but not for second generation pills .."; this is plainly wrong as Suissa did give such data in a clear and obvious table.
(8) He included both Jick 1995 and Jick 2000 in his original meta-analysis as he was unaware that the two studies had overlapping cases, although again that is clearly stated in the latter paper.
SECTION K: CONCLUSIONS ON THE FIRST ISSUE
|6||The Combined Oral Contraceptive.|
|11||The Regulatory History.|
|20||The Issues in the Litigation.|
|B||THE APPROACH TO DECIDING THE FIRST ISSUE|
|27||Case Control Studies.|
|36||Point Estimates and Confidence Intervals.|
|45||Aggregation of COC Products.|
|C||THE WHO STUDY|
|59||An a Priori Hypothesis?|
|64||All Centres or Oxford?|
|68||Hospital or GP Controls?|
|D||THE TNS: THE FIRST TWO STUDIES|
|81||The Origins of the Study.|
|84||The Progress of the Study.|
|98||The Mercilon Anomaly.|
|106||Duration of Use.|
|E||121TNS3 AND THE COX REGRESSION ANALYSIS|
|127||The Pill Calendar Data.|
|133||The Attack on Cox by Walker.|
|158||Walker's Separate Algebraic Attack.|
|159||Conclusion on Cox.|
|F||164THE JICK v FARMER DEBATE|
|165||The UK GPRD.|
|171||The Methods and Findings of the Studies.|
|185||The Development of the Issues.|
|194||Jick V: The Attack on Farmer's Controls.|
|G||THE OTHER STUDIES|
|255||Farmer 2000 "Pill Scare".|
|H||258BIAS AND CONFOUNDING|
|286||Conclusions on Prescriber, Diagnostic and Referral Bias.|
|287||Hidden Bias and Confounding.|
|288||Conclusions on Bias and Confounding.|
|298||Industry Funding Bias.|
|302||The Bradford Hill Criteria.|
|J||309||OVERVIEW OF THE STUDIES|
|K||339||CONCLUSIONS ON THE FIRST ISSUE|
THE CURRICULA VITARUM OF THE PRINCIPAL EXPERT WITNESSES
The Claimants' Witnesses
Alexander M. Walker. Qualified in medicine and holding a doctorate in epidemiology. Since 1991 Professor in the Department of Epidemiology at Harvard School of Public Health. Formerly Statistical Consultant New England Journal of Medicine. Contributing Editor "The Lancet" and Co-editor "Journal of Epidemiology and Bio-statistics". Author or Joint Author of over 200 articles, 5 dealing with risks associated with oral contraceptives. Currently on leave of absence from his academic chair. Employed by Ingenix Pharmaceutical Services, a commercial concern providing services in the field of epidemiology and public health.
Margaret Thorogood. A sociology graduate. Worked under Sir Richard Doll at Oxford University and gained a PhD based on a thesis studying the risk of fatal CV disease and OC use. Has published some 30 papers studying OC use and cardiovascular disease. Became Co-principal Investigator on the Transnational Study and was a member of the Publications Advisory Committee of the WHO. Collaborated on the MICA Study by the Drugs Safety Research Unit at Southampton into AMI and OC use.
Hershel Jick. A graduate of Harvard Medical School. Practised for a while in internal medicine and then moved to research in clinical pharmacology. Since the mid 1960s has been concerned in pharmacoepidemiology and with the BCDSP of which he has been director since 1971. His name appears on over 300 papers in learned journals all of which are concerned with health implications of diverse drugs. Under his direction the BCDSP holds a licence to use the UK GPRD based on which it has published very many drug studies.
Klim McPherson. Graduated in mechanical sciences and took a doctorate in medical statistics at the London School of Hygiene and Tropical Medicine. A University Lecturer in Medical Statistics at the University of Oxford, and from 1991 to 1996 Professor of Public Health Epidemiology at the LSHTM. Now Senior Scientist with the Medical Research Council at the Bristol Department of Social Medicine. A member of the CSM. A temporary member of the Sub-Committee of the CSM that considered the evidence in relation to the "Dear Doctor" letter of 1995.
Nicolas Dunn: Senior Lecturer in primary medical care at the University of Southampton. Fourteen years a General Practitioner. Senior Research Fellow in the Drug Safety Research Unit, Southampton. MSc and Diploma in Epidemiology. An author of a study in 1997 into myocardial infarction and OC use.
The Defendants' Witnesses
Samuel Shapiro: Qualified as a doctor in South Africa and practised in clinical medicine from 1957 to 1972 since when he has worked as an Epidemiologist. He worked in the BCDSP and from 1974 to 1999 at the Drug Epidemiology Unit at Boston University, retiring as its Director. Was Professor of Epidemiology at Boston University until June 2001. Now teaching at Columbia University in New York. 24 of the 306 papers to which his name is attached deal with the health risks of oral contraceptives.
Kenneth Duncan MacRae. Since 1969 a Bio-Statistician. 1976 1998 Senior Lecturer and Reader in Medical Statistics at Charing Cross and Westminster Medical School University of London. 1999 to 2002 Professor of Medical Statistics, Post-graduate Medical School, University of Surrey. Author of many published studies on epidemiology and bio-statistics, 13 of which relate to OC use and Cardiovascular illness.
Michael Lewis. Qualified in medicine in Germany. Holds a Diploma in Epidemiology from McGill University Canada where he was Assistant Professor of the Department of Epidemiology and Bio-Statistics 1993 to 1996 and Associate Director of Potsdam Institute of Pharmaco-Epidemiology and Technology Assessment. Currently Director and part owner of EPES a German commercial entity providing services in epidemiology principally to pharmaceutical companies. Senior Investigator in the Transnational Study.
Lothar Heinemann. Qualified in medicine in Germany. Professor for Preventive Medicine at the Academy of Sciences Berlin 1982. Adjunct Professor Epidemiology and Bio-Statistics at McGill University Canada 1993. Since 1990 Director of ZEG a commercial concern providing services in epidemiology and health research based in Berlin. A member of the WHO and TNS teams. Since 1993 has published 40 papers on the relationship between OC use and cardiovascular disease.
Richard Donald Trafford Farmer. Medically qualified, a Fellow of the Faculty of Public Health Medicine at the Royal College of Physicians. Previously Professor of Public Health Medicine at Charing Cross and Westminster Medical School. Currently Professor of Epidemiology at the Post-graduate Medical School at the University of Surrey. Since 1989 his published work mainly related to the epidemiology of suicide risks on public transportation systems. His publications relating to the cardiovascular effects of OC use started in about 1995 since when they have become the main focus of his interest.
APPENDIX 3 TABLE 1B PROFESSOR MACRAE'S OVERVIEW
APPENDIX 4REFERENCES TO THE RELEVANT SCIENTIFIC LITERATURE
(1) WHO collaborative study of cardiovascular disease and steroid hormone contraception. A multinational case-control study of cardiovascular disease and steroid hormone contraceptives. Description and validation of methods. Journal of Clinical Epidemiology 1995; 48: 1513-1547.
(2) Venous Thromboembolic disease and combined oral contraceptives: results of international multi-centre case-control study. Lancet 1995; 346: 1575 1582.
(3) Effect of different progestagens in low oestrogen oral contraceptives on venous thromboembolic disease. Lancet 1995; 346: 1582 1588.
(4) World Health Organisation. Cardiovascular disease and steroid hormone contraception. Report of WHO Scientific Group. WHO Technical Report Series 877; Geneva: 1998.
(5) Spitzer WO, Thorogood M, Heinemann L. Trinational case-control study of oral contraceptives and health. Pharmacoepidemiology and Drug Safety 1993; 2: 21 31.
(6) Lewis MA, Assmann A, Heinemann L, Spitzer WO. Interim review of the transnational case-control study of oral contraceptives and health: Approved protocol revisions through September 1995. Pharmacoepidemiology and Drug Safety 1996; 5: 43 51.
(7) Spitzer WO, Lewis MA, Heinemann LAJ, Thorogood M, MacRae KD. On behalf of the Transnational Research Group on Oral Contraceptives and the Health of Young Women. Third generation oral contraceptives and risk of venous thromboembolic disorders: An international case-control study. BMJ 1996; 312: 83 88.
(8) Lewis MA, Heinemann LAJ, MacRae KD, Bruppacher R, Spitzer WO, with the Transnational Research Group on Oral Contraceptives and the Health of Young Women. The increased risk of venous thromboembolism and the use of third generation progestogens: Role of bias in observational research. Contraception 1996; 54: 5 13.
(9) Alexander M Walker. Newer oral contraceptives and the risk of venous thromboembolism. Contraception 1998; 57: 169 181.
(10) Rosendaal FR. Venous Thrombosis: A multi-causal disease. Lancet; 353: 1167 1173.
(11) Suissa S, Spitzer WO, Rainville B, Cusson J, Lewis M and Heinemann L. Recurrent use of newer oral contraceptives and the risk of venous thromboembolism. Human Reproduction 2000; 15: 817 821.
(12) Suissa S, Blais L, Spitzer WO, Cusson J, Lewis M, Heinemann L. First time use of newer oral contraceptives and the risk of venous thromboembolism. Contraception 1997; 56: 141 146.
(13) Farley TM, Merik O, Marmot MG, Chang CO, Poulter NR. Oral contraceptives and the risk of venous thromboembolism: Impact of duration of use. Contraception 1998; 57: 61 65.
(14) Lewis M, MacRae K, Kuhl-Habich D, Bruppacher R, Heinemann L, Spitzer WO. The differential risk of oral contraceptives: The Impact of full exposure history. Human Reproduction 1999; 14: 1493 1499.
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(17) Jick H, Jick S, Derby L. Validation of information recorded on General Practitioner based computerised data resource in the UK. BMJ 1991; 302: 766 768.
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(20) Farmer R, Lawrenson R, Todd J, Williams T, MacRae K, Tyrer F, Leydon G. A comparison of the risk of venous thromboembolic disease in association with different combined oral contraceptives. British Journal of Clinical Pharmacology 2000; 49: 580 590.
(21) Jick H, Kaye J, Vasilakis C, Jick S. Risk of venous thromboembolism among users of third generation oral contraceptives compared with users of oral contraceptives with Levonorgestrel before and after 1995: Cohort and case-control analysis. BMJ 2000; 321: 1190 1195.
(22) Lawrenson R, Todd J, Leydon G, Williams T, Farmer R. Validation of the diagnosis of venous thromboembolism in general practice database study. British Journal of Clinical Pharmacology 2000; 49: 591 596.
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(34) Todd J, Lawrenson R, Farmer R, Williams T, Leydon G. Venous thromboembolic disease and combined oral contraceptives: A re-analysis of the MediPlus database. Human Reproduction; 14: 1500 1505.
(35) Neubauer R, Nortington R, Grubb G, Olsen A. GPRD epidemiology study on the use of oral contraceptives and the risk of cardiovascular events. Unpublished report, Wyeth-Ayerst Research. Philadelphia. 85 pages.
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(37) Sackett D. Bias in analytic research. J. Chron. Dis.; 32: 51 63.
(38) Dunn N, White I, Freemantle S, Mann R. The role of prescribing and referral bias in studies of the association between third generation oral contraceptives and increased risk of thromboembolism. Pharmacoepidemiology and Drug Safety; 7: 3 14.
(39) Heinemann L, Lewis M, Assmann A, Gravens L, Guggenmmoom-Holzmann I. Could preferential prescribing and referral behaviour of Physicians explain the elevated thrombosis risk found to associated with third generation oral contraceptives? Pharmacoepidemiology and Drug Safety; 5: 285 294.
(40) van Lunsen, H. Recent oral contraceptive use patterns in four European countries: Evidence for selective prescribing of oral contraceptives containing third generation progestogens. Eur. J. of Contraception and Rep. Health Care 1996; 1: 39 45.
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(49) Heinemann L, Lewis M, Assmann A, Thiel C. Case control studies on venous thromboembolism: Bias due to design? A methodological study of venous thromboembolism and steroid hormone use. Contraception 2002; 65: 207 214.
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(51) Hertz-Picciotto I. Invited commentary: Shifting the burden of proof regarding biases and low-magnitude associations. Am. J. of Epidemiology 2000; 151: 946 948.
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(53) Rosendaal F. Venous thrombosis: A multicausal disease. Lancet; 353:1167 1173.
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