These links may also be of interest;
http://scholar.google.com/scholar?hl=en&q=%22evidence+based%22+AND+
%28%22clinical+trial%22+OR+%22clinical+trials%22%29&btnG=&as_sdt=1%2C39
OR
http://tinyurl.com/l76fzpe
.
.
https://www.google.com/search?q=%22evidence+based%22+AND+(%22clinical+
trial%22+OR+%22clinical+trials%22)&hl=en&gws_rd=ssl#hl=en&q=%22evidence+
based%22+AND+(%22clinical+trial%22+OR+%22clinical+trials%22)&tbm=bks
OR
http://tinyurl.com/mqoqzac
.
.
http://temple.summon.serialssolutions.com/search?s.q=%22evidence+
based%22+AND+%28%22clinical+trial%22+OR+%22clinical+trials%22%
29&s.fvf%5B%5D=ContentType%2CNewspaper+Article%2Ct#!/search?ho=
f&fvf=ContentType,Newspaper%20Article,t&q=%22evidence%20based%22%
20AND%20(%22clinical%20trial%22%20OR%20%22clinical%20trials%22)&l=en
OR
http://tinyurl.com/mqupgor
.
.
.
Sincerely,
David Dillard
Temple University
(215) 204 - 4584
[log in to unmask]
http://workface.com/e/daviddillard
Net-Gold
http://groups.yahoo.com/group/net-gold
http://listserv.temple.edu/archives/net-gold.html
Research Guides
https://sites.google.com/site/researchguidesonsites/
SPORT-MED
https://www.jiscmail.ac.uk/lists/sport-med.html
http://groups.yahoo.com/group/sports-med/
http://listserv.temple.edu/archives/sport-med.html
On Fri, 1 Aug 2014, Stephen Senn wrote:
> The following paper may also be of interest
>
> Added Values
> http://onlinelibrary.wiley.com/doi/10.1002/sim.2074/abstract
>
> I distinguish between different questions one might hope to answer in a clinical trial
>
> Q1. Was there an eff?ect of treatment in this trial?
> Q2. What was the average eff?ect of treatment in this trial?
> Q3. Was the treatment eff?ect identical for all patients in the trial?
> Q4. What was the eff?ect of treatment for di?erent subgroups of patients?
> Q5. What will be the eff?ect of treatment when used more generally (outside of the trial)?
>
> and state
>
> "Given an assumption of what might be called local (or weak) additivity, that is to say
> that the eff?ect of treatment was identical for all patients in the trial (in other words that the
> answer to Q3 is ‘yes’), then Q1, Q2, & Q4 can all be answered using the same analysis: a
> con?dence interval or posterior distribution for the mean eff?ect of treatment says it all. The
> eff?ect on each patient is the average e?ffect Q2 and is hence the eff?ect in every subgroup Q4
> and if it is implausible that this eff?ect is zero, then the treatment has an e?ffect Q1. Given
> a further assumption of universal (or strong) additivity, this observed eff?ect is the e?ffect to
> every patient to whom it might be applied; this also provides an answer to Q5.""
>
> Stephen
>
> _____________________________________________________________________________________________________________________________________________
> From: Amy Price [[log in to unmask]]
> Sent: 31 July 2014 23:41
> To: 'Huw Llewelyn [hul2]'; Stephen Senn; 'Benjamin Djulbegovic'
> Cc: 'Michael Power'; [log in to unmask]; 'Kevork Hopayian'
> Subject: RE: Since when did case series become acceptable to prove efficacy?
>
> I agree Huw and thank you Senn for your clarifications. I am keeping this stream of communication, it is important to see things through the
> eyes of those that write research up for the times when standardization in communication fails us. I have seen areas that have contributed to
> a less than clear understanding because of my own thinking/background and really appreciate this exchange.
>
>
>
> Best
>
> Amy
>
>
>
> From: Huw Llewelyn [hul2] [mailto:[log in to unmask]]
> Sent: 31 July 2014 05:21 PM
> To: Stephen Senn; 'healingjia Price'; Benjamin Djulbegovic
> Cc: 'Michael Power'; [log in to unmask]; 'Kevork Hopayian'
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Perhaps the most interesting thing about this discussion is that the same topic of hypothesis testing regarding RCTs is seen from such very
> different perspectives by people trained in different disciplines!
>
> Huw.
>
>
> _____________________________________________________________________________________________________________________________________________
>
>
> From: Stephen Senn <[log in to unmask]>
>
> Date: Thu, 31 Jul 2014 20:42:17 +0200
>
> To: 'healingjia Price'<[log in to unmask]>; 'Djulbegovic, Benjamin'<[log in to unmask]>
>
> Cc: 'Huw Llewelyn [hul2]'<[log in to unmask]>; 'Michael Power'<[log in to unmask]>; <[log in to unmask]>; 'Kevork
> Hopayian'<[log in to unmask]>
>
> Subject: RE: Since when did case series become acceptable to prove efficacy?
>
>
>
> There seem to be a lot of things being discussed in this thread. I have four comments.
>
> 1) The main purpose of the falsificationism paper was to show that there was a fundamental difference in trying to disprove the
> hypothesis that the data comes from a single distribution (e.g. the drug is a placebo) and trying to disprove the hypothesis that the data
> come from two distributions (the interventional drug is not the same as the active comparator). The latter case is what you try to do in
> active control equivalence studies. If you reject the two distribution theory, then you end up with one distribution and the conclusion that
> the new treatment is equivalent to the old. (This is seen most clearly in bioequivalence studies but it applies elsewhere also.) The point of
> that paper was to claim that all the statistical fixes in the world do not deal with the fundamental ‘philosophical’ difference between these
> two cases. Some of the technical issues are currently being debated on Deborah Mayos’ blog. See
>
> http://errorstatistics.com/2014/06/05/stephen-senn-blood-simple-the-complicated-and-controversial-world-of-bioequivalence-guest-post/
>
> and
>
> http://errorstatistics.com/2014/07/31/roger-berger-on-senns-blood-simple-with-a-response-by-s-senn-guest-posts/
>
>
>
> 2) 95% of (correctly calculated) 95% confidence intervals will contain the true parameter value. This does not mean (however), for
> example, that 95% of CIs that exclude 0 do so correctly. One must beware of invalid inversion.
>
>
>
> 3)The case series method, as pioneered by Farrington and Whittaker
>
> Farrington CP, Whitaker HJ. Semiparametric analysis of case series data (with discussion). Journal of the Royal Statistical
> Society Series C-Applied Statistics 2006; 55: 1-28.
>
>
>
>
>
> and the earlier case cross-over method of Marshall et al
>
> Marshall RJ, Jackson RT. Analysis of case-crossover designs. Statistics in Medicine 1993; 12: 2333-2341.
>
>
>
> can be powerful ways of assessing causality using the timing of events.
>
> Even where we have clinical trials, there are occasions where it is clear that we would not accept the results that the pure randomisation
> analysis would produce. Such a case is given by the trial of TGN1412 in which 6 out of 6 healthy volunteers given TGN1412 had severe
> reactions and 2 given placebo did not. A Fisher’s exact test of the result does not begin to describe what everybody. This trial and a much
> larger one where it would be foolish to depart from classical analysis are discussed here
>
> Senn S. Lessons from TGN1412 and TARGET: implications for observational studies and meta-analysis. Pharmaceutical statistics 2008; 7:
> 294–301.
>
> However, it is not clear to me from this discussion that case-series methodology is being appropriately applied in the example cited.
>
> 4)Picking up on an earlier thread, one has a natural prejudice in favour of one’s own work but I think it would be wise to defer judgement on
> Tamiflu until (at least) the MUGAS analysis reports http://www.mugas.net/mugas/re-analysis-of-clinical-trials/
>
> .
>
>
>
> My declaration of interest is here
>
> http://www.senns.demon.co.uk/Declaration_Interest.htm
>
>
>
>
>
> Stephen
>
>
>
> From: healingjia Price [mailto:[log in to unmask]]
> Sent: 31 July 2014 16:21
> To: Djulbegovic, Benjamin
> Cc: Huw Llewelyn [hul2]; Michael Power; [log in to unmask]; Kevork Hopayian; [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Thank you for the precision. It clarifies how error of thought can creep in through careless phrasing especially illuminating as we are
> dealing with uncertainty.
>
>
>
> Is there a link on the CI statement Ben as I would like to understand this better. Are you saying that the single computed 95% is
> dichotomous and as a result can't be between something because we have already established the95%?
>
>
>
> Best
>
> Amy
>
> Amy Price
>
> Empower 2 Go
>
> Building Brain Potential
>
> Http://empower2go.org
>
> Sent from my iPad
>
>
> On 31 Jul 2014, at 07:04 am, "Djulbegovic, Benjamin" <[log in to unmask]> wrote:
>
> Agree with Huw.
>
> We have to ask our selves where the laws come from- presumably from testing multiple hypotheses over time resulting in what Quine
> called "web of knowledge". ( I think we may have been confusing here the difference between hypotheses, theories, and laws - admittedly
> not easy definition to give in a short reply)
>
> Ben
>
>
>
> PS. BTW, the 95% CI does not say that the true values are between x and y ; instead, the frequency with which this single computed 95%
> CI contains the true value is either 100% or 0%.
>
>
> Sent from my iPad
>
> ( please excuse typos & brevity)
>
>
> On Jul 31, 2014, at 3:15 AM, "Huw Llewelyn [hul2]" <[log in to unmask]> wrote:
>
> Hi Michael
>
> I agree that the null hypothesis is a device to help estimate the probability of replicating a result using multiple
> readings eg of an RCT. But that RCT will be based on an underlying hypothesis eg that the treatment molecule is able to
> compete with an endogenous molecule for a receptor and thus improve a patient's symptoms. This interaction would be based
> partly on the mathematical model representing a general law called 'the law of mass action'.
>
> If the RCT fails to show a replicable difference in symptoms between this molecule and a placebo then the entire reasoning
> leading up to the RCT, (including the general 'law of mass action') is called into question. Popper appears to say that the
> whole theory / hypothesis is 'falsified'. I prefer to say that it is thrown into doubt and that the probability of success
> of a hypothesis using that rationale in future is lower.
>
> It is possible that some error was made eg that the molecule used in the RCT was not manufactured properly and different to
> the one used in earlier phases of its development. If this supplementary hypothesis is 'verified', and the correct molecule
> is used in a second RCT which does show a difference which can probably be replicated, then the probability of the original
> hypothesis / theory will be restored.
>
> What do you think of this?
>
> Best
>
> Huw
>
>
> _____________________________________________________________________________________________________________________________________________
>
>
> From: Michael Power <[log in to unmask]>
>
> Sender: "Evidence based health (EBH)" <[log in to unmask]>
>
> Date: Thu, 31 Jul 2014 06:34:44 +0100
>
> To: <[log in to unmask]>
>
> ReplyTo: Michael Power <[log in to unmask]>
>
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
>
>
> Hi
>
>
>
> Apologies about but-ing into this conversation so late. But, sometimes philosophy seems to me to make things so complicated that
> practical understanding disappears.
>
>
>
> An RCT comparing the effects of treatments A and B does not test any theory analogous to a general law such as F = MA.
>
>
>
> A clinical trial is simply a measuring tool, a tool for measuring effects
>
>
>
> The null hypothesis is a way of framing the statistical theory that underpins the measurement of random variation: If the RCT
> were to be repeated endlessly, the 95% confidence interval(s) it has measured will “capture” the true measured mean 95% of the
> time.
>
>
>
> This is about precision, not accuracy. I.E. the 95% CI captures the true measured mean, NOT the true mean.
>
>
>
> The difference between the true mean and the true measured mean is the bias, or systematic error of the measurement tool, and is
> a consequence of the accuracy of the measuring instrument.
>
>
>
> We can measure precision. But we cannot measure bias, we can only estimate it by critical appraisal (not by deduction as Stephen
> Senn’s 1991 paper would have us believe).
>
>
>
> So, there are 3 fundamental problems of induction:
>
>
>
> 1. Trials measure precision, but our heads see the measurements as accurate – this is a psychological problem, which
> hopefully can be mitigated by education
>
> 2. Trial design (e.g. control, randomization, blinding) can hopefully mitigate the risks of bias. And, critical appraisal
> can guestimate the risks of bias. But, because important bias can arise from sources we can’t control or can’t imagine, our
> mitigations and guestimates leave an uncertain interval of fuzziness around any measurement. Bias can only be measured against a
> true reference standard, but we are forced to use an artificial “gold standard”, and we know from experience that the gold can
> turn out to be fool’s gold. Conclusion: we need outside evidence to calibrate the accuracy of measurements of clinical trials
> (which will have the Bayesians clapping their hands in joy).
>
> 3. We have evidence of mean (measured) effects and guestimates of risks of bias. How do we apply this evidence to the
> individual in the consultation? This is nowhere near the problem of betting on whether the sun will rise tomorrow, or if E=MC^2
> has to be applied to F = MA when calculating the tides or electron orbitals. (Do I hear the Bayesians again?)
>
>
>
> I hope I have falsified the hope of falsification in RCTs!
>
>
>
> Michael
>
>
>
>
>
>
>
> From: Evidence based health (EBH) [mailto:[log in to unmask]] On Behalf Of Djulbegovic, Benjamin
> Sent: 31 July 2014 00:31
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Hi Huw,
>
> Your e-mail succinctly summarizes the epistemological problems that have been debated in science for hundred of years going all
> the way to Aristotle! Indeed, the problem of application of probability calculus to single events is one of the eternal issues.
> The usually proposed solution is to accept the premise of exchangeability of past with future events- whether this assumption is
> always acceptable is another issue, but so far, it has served us pretty well.
>
> I look forward to hearing further thoughts from you and others on these issues that are more relevant to EBM that people may
> appreciate at first blush..
>
> Best
>
> Ben
>
>
> Sent from my iPad
>
> ( please excuse typos & brevity)
>
>
> On Jul 30, 2014, at 6:23 PM, "Huw Llewelyn [hul2]" <[log in to unmask]> wrote:
>
> Dear Amy, Ben, Kev, Stephen and all
>
> Thank you Ben for attaching a link to Stephen Senn's paper. I would be grateful for your comments on the questions
> that I pose below to try to clarify my understanding.
>
> If I postulate (or ‘hypothesise’) that it will probably rain tomorrow and it does rain then is my ‘rain hypothesis’
> verified and is the alternative ‘no rain hypothesis’ falsified? Do you think that this use of the term ‘hypothesis’,
> ‘verified’ and ‘falsified’ for a single event is appropriate?
>
> If I postulate that it will probably rain tomorrow, I may look for more facts which make it more probable or less
> probable that it will rain. If a null hypothesis that it will be sunny becomes very improbable, I can decide to
> ‘reject’ the plan of going to the sea-side tomorrow to ‘sun’ myself. Note that the null hypothesis does not include
> all the other possibilities e.g. ‘not sunny but dry’. Do you agree that we can never verify or falsify a statistical
> hypothesis about an infinitely large population by direct observation but only estimate its probability?
>
> The problem with a scientific hypothesis, theory or diagnosis is that it is not like a single prediction about a
> statistical null hypothesis about an unobservable infinite population or an easily accessible falsifiable or
> verifiable hypothesis about tomorrow’s rain. It is a title to a group of predictions about past, present and future
> consequences, many of which are interconnected and the probability of many of which cannot easily be estimated
> directly by studies. The result of a single RCT on an infinite number of patients is one of these consequences that
> we can try to predict from a study sample. Popper appears to say that if one such a consequence becomes improbable,
> then the overall hypothesis / theory is 'falsified'. However, to my mind the validity of the overall hypothesis /
> theory becomes less probable and an alternative hypothesis / theory may become more probable. A resulting decision
> to reject one course of scientific investigation and to pursue another is another matter. Popper points out that
> even if all the consequences do remain probable after testing, we still cannot assume that the overall hypothesis /
> theory is verified (as I assume there may be other consequences and alternative hypotheses / theories that we have
> not yet considered). It seems to me that our imaginary model is a hypothesis when there is an intention to test it
> against some alternative but a theory if there is no immediate intention to do so. Do you agree?
>
> Best
>
> Huw
>
>
> _____________________________________________________________________________________________________________________________________________
>
>
> From: Evidence based health (EBH) [[log in to unmask]] on behalf of Amy Price [[log in to unmask]]
> Sent: 30 July 2014 20:14
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
> Thanks Ben and Kev,
>
>
>
> I found paragraph 2 of Kev’s explanation helpful. I used to not love theory and think it took too much room in the
> bathwater. After throwing that baby out I have searched for it. I came to the conclusion that theory became difficult when
> it was overstated and built on as if it was a validated fact without uncertainties and so it was not the theory that was
> the issue but the abuse of it. I have defined in my own mind the term pragmatic to see if something works and at what
> dosage/intensity etc and explanatory to define why and to improve the working. To me it is a cycle not an either or
> superiority. The problem comes with expecting more than the design can support.
>
>
>
> Best
>
> Amy
>
>
>
> From: Evidence based health (EBH) [mailto:[log in to unmask]] On Behalf Of Djulbegovic, Benjamin
> Sent: 30 July 2014 02:37 PM
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Perhaps, this paper to which I alluded before may help clarify some of the issues we are discussing
>
>
>
> Senn SJ. Falsificationism and clinical trials. Stat Med. 1991;10:1679-1692.
>
>
>
> Stephen used to be active on this group, perhaps he may wish to comment…
>
>
>
> Best
>
> ben
>
>
>
>
>
> From: Evidence based health (EBH) [mailto:[log in to unmask]] On Behalf Of k.hopayian
> Sent: Wednesday, July 30, 2014 5:08 AM
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Dear Ben and all,
>
> To those who dislike theory, at least please read the next paragraph,
>
>
>
> 1 This discussion is important because of its practical consequences. Many people outside EBP mistakenly believe that EBP
> holds that anything less than a clinical trial is poor evidence. So comparing RCTs to the method of basic science that
> develops theories can give support to these mistaken beliefs. (That is not to say that you, Ben, are mistaken).
> Observational studies are no less scientific (in the sense of applying statistics, medical knowledge, pharmacology etc)
> than RCTs, they both use the tools of epidemiology, it is the risk of bias that differs.
>
>
>
> 2 I would argue that the RCT process has a superficial resemblance to the Popperian method: Null hypothesis - Experiment -
> Reject/Do not reject null hypothesis; Theory - Prediction - Experiment -Reject/Do not reject theory.
>
> The difference is that theories attempt to explain observations already made and then predict new observations for testing.
> The null hypothesis does not explain current observation nor predict new observations. It applies theories that do. The use
> of the word explanatory in the explanatory vs pragmatic variation of trials only adds to the superficial resemblance, an
> example maybe of what a contemporary of Popper said, that philosophy is the battle against bewitchment by language.
>
>
>
> No, it isn't fall yet but the Parrottia persica outside my front door proudly displays leaves of varying shades. It was a
> bare, straggly, ugly piece of bark when I planted it. Five years later, it is an admirable exhibit.
>
>
>
> Good luck with the grant application!
>
>
>
> Kev
>
>
>
> On 26 Jul 2014, at 15:38, Djulbegovic, Benjamin <[log in to unmask]> wrote:
>
>
>
> This is “learning ” weekend for me, Kev
>
> Working on the grant (what else is new?) and my 99% of perspiration is on welcome occasions being alleviated by reflection
> on thoughtful messages and remarks by people like you…(I confess: when I get tired of writing, I log back on my e-mail, and
> the messages from the EBM folks never stop inspiring me…)
>
>
>
> In thinking about your latest example, we may be talking about two different things: evidence vs. decision-making, which in
> clinical trial design paradigm translates into explanatory trials (whose goal is to provide a scientific answer to a
> research question, typically focusing on the proof of a concept or mechanism etc ;‘Efficacy” question) vs. pragmatic trials
> (Which treatment of already proven efficacy is better?” ;“effectiveness question). [Several years ago we used regret
> approach to tackle these issues; see:Hozo I, Schell MJ, Djulbegovic B. Decision-making when data and inferences are not
> conclusive: risk-benefit and acceptable regret approach. Semin Hematol. Jul 2008;45(3):150-159.]
>
> In terms of application of Popper’s discourse of scientific method to clinical trials, Jeremy Howick informed me that
> Fisherian hypothesis testing and Popperian falsificationism is identical. Fisher wrote it first, but Popper had not read
> Fisher (until much later, I believe) at which point Popper acknowledged the similarity… (I slightly edited Jeremy’s words,
> and if I am not quoting him accurately, I hope he can clarify)
>
>
>
> Enjoy auburn leaves (is it already fall in England?)
>
> Best
>
> ben
>
>
>
>
>
>
>
> From: Evidence based health (EBH) [mailto:[log in to unmask]] On Behalf Of k.hopayian
> Sent: Saturday, July 26, 2014 7:47 AM
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
> Hi Ben,
>
>
>
> Short reply: I respectfully disagree that a trial is an example of Popper's scientific method. Popper was concerned
> with theory. Whether drug A is better than B is not a theory (although confusingly, the negation of that statement is
> called the null hypothesis) in the sense that the biochemistry and pharmacology around those drugs have theories (such as
> drug receptors, enzyme action etc).
>
>
>
>
>
> Slightly longer reply: Theories make predictions but not all predictions come from theories.
>
> For example, the laws of physics are applied in engineering. Physics and engineering have theories. Engineers may design
> cars. Two cars may be compared for performance (acceleration, speed, efficiency etc). In comparing them, a manufacturer may
> start with an idea (our cars are better than yours) but that would hardly count as a theory. [By the way, have car
> manufacturers ever ever started with a null hypothesis?:-)] The manufacturer's prediction may be proven wrong (and no doubt
> get buried in company vaults, car manufacturers are so different to pharma, aren't they?) but no rejection of the theory of
> engineering is necessarily implied. Now if an engineer designed a car whose performance was beyond the boundaries predicted
> by the laws of thermodynamics, that WOULD falsify theory.
>
>
>
> It is a lovely sunny weekend here in Suffolk, with many shades of green and auburn leaves, so out I go. I hope your weekend
> is a good one too.
>
>
>
>
>
>
>
> Dr Kev (Kevork) Hopayian,
>
> MD FRCGP
> General Practitioner, Leiston, Suffolk,
>
> General Practice Trainer, Leiston
>
> Hon Sen Lecturer, Norwich Medical School, University of East Anglia
> Primary Care Tutor, East Suffolk
>
> RCGP Clinical Skills Assessment examiner
>
> NHS Senior Appraiser, East Anglia
>
> http://www.angliangp.org
>
>
>
> On 24 Jul 2014, at 23:40, Djulbegovic, Benjamin <[log in to unmask]> wrote:
>
>
>
> Kev,
>
> In fact, clinical trial is a classic example of (Popper's) falsificationism paradigm...and does test hypothesis that one
> drug is better than the other ( Ho: A=B; Ha:A<>B, as postured by classic frequentist statistical approach). Statistical
> evidence obtained this way connects one phenomena with others eventually corroborating ( or, rejecting) theories ( group
> of related principles and laws that were built by testing a number of hypotheses) such as those if beta-blockers effects
> are consistent with biochemical drug-receptor theory...
>
> Best
>
> Ben
>
> Ps Steven Senn had a wonderful article some years ago about falsificationism in clinical trials...worth reading...
>
>
>
>
> Sent from my iPad
>
> ( please excuse typos & brevity)
>
>
> On Jul 24, 2014, at 5:06 PM, "k.hopayian" <[log in to unmask]> wrote:
>
> "The definition of breakthrough is "it costs a packet" " Now that, I like..
>
>
>
> But I have to disagree on your method of science. Einstein's general relativity theory remains a theory despite the
> experimental results that concord with the predictions it makes. What these experiments do is fail to falsify the
> theory, so we stick with it. There are some things it cannot explain, which quantum theory does better, so we
> continue with two not compatible but very useful models to explain our world.
>
>
>
> Such models and experiements should not be confused with the method employed in trials. Trials are not designed to
> test a theory (for example, a trial of betablockers is not testing the theory that there are biochemical receptors).
> The trial is there to establish which of one or more interventions is superior, if at all. No theory/modle is
> falsified by such experiments - although beliefs (some cherished) can be dispelled. I suppose
> statisticians/epidemiologists have not helped our understanding by using the term hypothesis testing.
>
>
>
> Kev
>
>
>
>
>
>
>
> Dr Kev (Kevork) Hopayian,
>
> MD FRCGP
> General Practitioner, Leiston, Suffolk,
>
> General Practice Trainer, Leiston
>
> Hon Sen Lecturer, Norwich Medical School, University of East Anglia
> Primary Care Tutor, East Suffolk
>
> RCGP Clinical Skills Assessment examiner
>
> NHS Senior Appraiser, East Anglia
>
> http://www.angliangp.org
>
>
>
> On 24 Jul 2014, at 20:49, Tom Jefferson <[log in to unmask]> wrote:
>
>
>
> The definition of breakthrough is "it costs a packet" - and Sovaldi fits the picture.
>
> This kind of bullshit is replicated in the EU with so called early assessment to get better, innovative drugs earlier
> to patients who desperately need them. So the burden of proof is slowly being pushed back to phase IV or beyond which
> may be observational, subverting Galileo's methods.
>
> What we should always remember is that Einstein's general relativity theory (1915) was a theory and remained a theory
> until Eddington's natural experiment during the 1919 solar eclipse confirmed that gravitation could deflect starlight
> as the theory had put forward.
>
>
>
> The rise of observational data (even non comparative) is an involution, not an evolution. There are many culprits
> most of them in my profession (I am a physician) and they will be held to account.
>
> Greed and science do not mix.
>
> Nite from Rome.
>
> Tom.
>
>
>
> On 24 July 2014 17:10, Poses, Roy <[log in to unmask]> wrote:
>
> Thanks, Tom. Could not agree more. But it seems like there is little protest about this paradigm shift, your work,
> of course, excepted.
>
> Re: "trials are for regulators" - but in the US, the regulators apparently decided they don't need so many trials.
> The FDA designated Sovaldi/ sofosbuvir as a "breakthrough" therapy, which apparently allows approvals based on much
> more limited evidence, although the evidence behind that "breakthrough" designation itself was not clear.
>
> See: http://www.fda.gov/newsevents/newsroom/pressannouncements/ucm377888.htm
>
>
>
> On Thu, Jul 24, 2014 at 10:45 AM, Tom Jefferson <[log in to unmask]> wrote:
>
> Roy and all evidencers.
>
> The scientific method of Galileo has been subverted before our very eyes.
>
> Galileo observed, described and then produced a hypothesis or theory which he then proceeded to test with an
> experiment. This model has served us well in the last 400 years with a few exceptions (the already cited
> penicillin for example).
>
> What we now witness is a fundamental subversion of the order (I am not going to call it a paradigm shift) of
> things. Observations are fact, case-controls, case series, cohorts (even retrospective and datalinked ones) are
> being held out as proof. Trials are for regulators, they say.
>
> The origin of all this is complex and partly known. In the Tamiflu story as we began uncovering the extent of
> reporting bias affecting the clinical trials that had been used to make policy and justify stockpiling,
> decision makers turned to observational evidence (of universally recognised poor quality) as props for their
> unchangeable policies.
>
> It is a sad parable of the world we live in.
>
> Best wishes,
>
> Tom.
>
>
>
> On 24 July 2014 16:33, Valerie King <[log in to unmask]> wrote:
>
> Agree Roy.
>
>
>
> Don’t think we can assume, based on these case-series in highly selected populations, that the “eradication”
> rate is >=90% or that SVR is a good surrogate. Also, although the studies were registered with SVR24 as primary
> outcome the FDA let them give SVR12 as part of the “breakthrough” designation so we don’t even have a
> particularly good surrogate.
>
>
>
> Virtually all of the subjects in published studies had very positive treatment prognosis anyway. Over half of
> subjects had HCV genotype 2 which is the easiest to treat no matter what drug used. And there is certainly
> more than a hint in several of the studies of substantial relapse rates after SVR24 achieved (e.g. ~9% in
> NUTRINO.) I honestly think that most people are listening to the marketing drumbeat on this drug and not
> reading the papers for themselves. I’d be happy to have these drugs be the breakthrough that most people seem
> to think that they are, but in my opinion, currently there are a lack of data to support that position.
>
>
>
> Cheers,
>
> Valerie
>
>
>
> Valerie J. King, MD, MPH
>
> Professor of Family Medicine, and
>
> Public Health & Preventive Medicine
>
> Director of Research
>
> Center for Evidence-based Policy
>
> Oregon Health & Science University
>
> Mailstop MDYCEBP
>
> Suite 250
>
> 3030 SW Moody Ave.
>
> Portland, OR 97201
>
> Voice: 503-494-8694
>
> Fax: 503-494-3807
>
> [log in to unmask]
>
> www.ohsu.edu/policycenter/
>
> Twitter: @drvalking
>
>
>
>
>
>
>
> From: Evidence based health (EBH) [mailto:[log in to unmask]] On Behalf Of Poses, Roy
> Sent: Thursday, July 24, 2014 07:08
>
>
> To: [log in to unmask]
> Subject: Re: Since when did case series become acceptable to prove efficacy?
>
>
>
>
>
> But it is not clear that SVR is a good surrogate marker.
>
>
>
> See: http://www.thelancet.com/journals/lancet/article/PIIS0140-6736%2814%2961025-4/fulltext
>
> and the Cochrane review it references:
>
> http://www.ncbi.nlm.nih.gov/pubmed/24585509
>
>
>
> As an aside, given that hep C infection is a chronic problem and bad effects from it occur long after original
> infection, it is extremely strange that no one has ever thought to do a good RCT with long term follow up to
> assess clinical outcomes of ANY hepatitis C treatment.
>
>
>
> On Wed, Jul 23, 2014 at 4:54 PM, Djulbegovic, Benjamin <[log in to unmask]> wrote:
>
> But, if eradication of viral load is greater than 90% ( and we accept viral load as a good surrogate marker),
> would then single arm study be justified?
>
> Ben
>
> Sent from my iPhone
>
> (Please excuse typos & brevity)
>
>
> On Jul 23, 2014, at 4:50 PM, "Poses, Roy" <[log in to unmask]> wrote:
>
> That seems reasonable, but certainly does not apply to this particular clinical situation and
> article.
>
>
>
> On Wed, Jul 23, 2014 at 4:47 PM, Steve Simon, P.Mean Consulting <[log in to unmask]> wrote:
>
> On 7/23/2014 9:39 AM, Poses, Roy wrote:
> > I still don't see why case-series without any control groups are now
> > regarded as credible ways to evaluate efficacy of therapy???
>
> I cannot comment on this particular example, but in general you can safely dispense with a control group
> when there is close to 100% morbidity or mortality in that control group. In such a setting, any
> improvement is painfully obvious and does not need a rigorous design or fancy statistical analysis. Also,
> it is pretty difficult and probably unethical to randomly assign half your patients to be in a group that
> has 100% morbidity or mortality.
>
> Steve Simon, [log in to unmask], Standard Disclaimer.
> Sign up for the Monthly Mean, the newsletter that
> dares to call itself average at www.pmean.com/news
>
>
>
>
> --
>
> Dr Tom Jefferson
> Medico Chirurgo
> GMC # 2527527
> www.attentiallebufale.it
>
>
>
>
> --
> Roy M. Poses MD FACP
> President
> Foundation for Integrity and Responsibility in Medicine (FIRM)
> [log in to unmask]
> Clinical Associate Professor of Medicine
> Alpert Medical School, Brown University
> [log in to unmask]
>
>
>
>
> --
> Dr Tom Jefferson
> Medico Chirurgo
> GMC # 2527527
> www.attentiallebufale.it
>
>
>
>
>
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