Martin
--
***************************************************
J. Martin Bland
Prof. of Health Statistics
Dept. of Health Sciences
Seebohm Rowntree Building Area 2
University of York
Heslington
York YO10 5DD
Email: mb...@york.ac.uk
Phone: 01904 321334
Fax: 01904 321382
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retrospective power
Luiz
Luiz Alberto S Melo Jr
Dept of Ophthalmology
Federal University of Sao Paulo
Brazil
Martin
kornbrot wrote:
> I tried ‘retrsopective power’ in google
> Following may be useful:
> http://statpages.org/postpowr.html
> How to do it with link to ms by lnth on why NOT to do it
> Wikipeadia
> http://wiki.math.yorku.ca/index.php/Statistics:_Post_hoc_power_analysis
>
> 1. Zumbo, B.D. and A.M. Hubley, /A Note on Misconceptions Concerning
> Prospective and Retrospective Power./ Journal of the Royal Statistical
> Society: Series D (The Statistician), 1998. *47*(2): p. 385-388.
> May be too technical for your intended audience?
>
> Best
>
> diana
>
> On 15/11/07 09:32, "Bland, M." <mb...@york.ac.uk> wrote:
>
> retrospective power
>
>
>
> *Professor Diana Kornbrot
> *School of Psychology
> University of Hertfordshire
> College Lane, Hatfield, Hertfordshire AL10 9AB, UK
>
> email: _d.e.k...@herts.ac.uk_
> web: _http://web.mac.com/kornbrot/iweb/KornbrotHome.html_
> voice: +44 (0) 170 728 4626
> fax: +44 (0) 170 728 5073
> *Home
> *19 Elmhurst Avenue
> London N2 0LT, UK
>
> voice: +44 (0) 208 444 2081
> fax: +44 (0) 870 706 4997
>
>
>
>
>
--
SR Millis
--- "Bland, M." <mb...@york.ac.uk> wrote:
> Can anybody suggest a good reference for the
> non-statistician about why
> retrospective power calculations should not be done?
> I recall this
> being discussed in the past.
Scott R Millis, PhD, MEd, ABPP (CN,CL,RP), CStat
Professor & Director of Research
Dept of Physical Medicine & Rehabilitation
Wayne State University School of Medicine
261 Mack Blvd
Detroit, MI 48201
Email: smi...@med.wayne.edu
Tel: 313-993-8085
Fax: 313-966-7682
This reference may be illustrative of the” movement” referred to below:
Anthony J. Onwuegbuzie and Nancy L. Leech. Post Hoc Power: A Concept Whose Time Has Come. Understanding Statistics 3 (4):201-230, 2004.
John L Moran
Department of Intensive Care Medicine
The Queen Elizabeth Hospital
28 Woodville Road
Woodville SA 5011
Australia
Tel 61 08 82227464
Fax 61 08 2226045
Mobile 0414 267 529
E-mail: john....@adelaide.edu.au
_____________________________________________________
Doug Altman
Professor of Statistics in Medicine
Centre for Statistics in Medicine
Wolfson College Annexe
Linton Road
Oxford OX2 6UD
email: doug....@cancer.org.uk
Tel: 01865 284400 (direct line
01865 284401)
Fax: 01865 284424
www:
http://www.csm-oxford.org.uk/
EQUATOR Network - resources for reporting research
www:
http://www.equator-network.org/
>I don't know how different it might be from their 2004 publication. Nor
>have I had time to read this paper, but it is clear that they advocate
>post hoc power calculations when results are non-significant. I would take
>some persuading that this is a sensible idea.
I guess I'm asking for trouble by expressing this view, but I am a little
heartened to see that I am probably not totally alone.
I see no need for post-hoc power calculations for consumption by
Statisticians; for them, confidence intervals should tell them all they
need to know. However, in the specific case in which:
(a)...the results are 'non-significant', but of a magnitude at least as
great as the 'design value' for the trial
AND
(b)...it transpires that the initial sample size estimation was based on an
under-estimate of variability
... then, I think that post-hoc power calculations may provide a better way
to convey to non-statisticians 'what went wrong'. From the investigator's
viewpoint, they were advised that (on the basis of available information) a
certain sample size would give them a high (say 90%) chance of detecting
their 'minimum efffect of interest' as significant. Having undertaken a
trial of the size advised and finding a treatment effect greater (perhaps
much greater) than that 'minimum effect of interest', they may well have
some difficulty in understanding 'what went wrong'. One could explain the
reason (variability mucht greater than predicted) and even try to
illustrate it with CIs, but I suspect that the explanation they would find
most easy to understand was that, with the benefit of hindsight (knowledge
of the actual variability encountered) the trial of that sample size had
only a much lower chance (quantified by the post-hoc power calculation) of
detecting 'as significant' an effect of that magnitude.
So, in that particular situation, I do see some merit and justification (in
terms of 'communication') in undertaking a post-hoc power calculation - but
I dare say that many/most will probably disagree!
Kind Regards,
John
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Which is:
1) not correct
2) the likely message that gets across to clinicians
Hence you have provided an excellent argument why post-hoc power
calculations should not be performed.
Best,
Bendix Carstensen
> -----Original Message-----
> From: MedS...@googlegroups.com
> [mailto:MedS...@googlegroups.com] On Behalf Of John Whittington
> Sent: 19. november 2007 15:51
> To: MedS...@googlegroups.com
> Cc: MedS...@googlegroups.com
> Subject: {MEDSTATS} Re: retrospective power calculations
>
>
>John,
>It seems to me that you implicitly assume that another adequately
>powered trial would yield the same point estimate and just a narrower
>c.i. than the current one.
>Which is:
>1) not correct
>2) the likely message that gets across to clinicians
>Hence you have provided an excellent argument why post-hoc power
>calculations should not be performed.
I don't think I was making that assumption. That is why I was careful to
speak in terms of 'chances' (i.e. probability/power) of getting a
significant result, not a guarantee that an adequately-powered trial
definitely _would_ have produced a significant result (of any mean magnitude).
So, I'm certainly NOT suggesting that investigators should be led to
believe that they would necessarily have got a 'significant' result (of the
same magnitude or whatever) had they conducted a trial with a sample size
calculated using a 'crystal ball' - and I would be at pains to make sure
that they did not get that impression. However, in answer to their
question about 'what went wrong', it seems to me very reasonable to
demonstrate that, 'with what we now know', it would never have been
suggested that the sample size used would be adequate to give a reasonable
power ('chance of detecting a result as significant').
I would say much the same in relation to any crucial (non-statistical)
assumptions which went into the trial design which proved to have been
incorrect. Again, without making any suggestions about what the result
would have been if correct assumptions had been made, I would want to point
out that we would never have considered the study as designed to be
adequate/satisfactory if we had known 'what we know now'.
I bet that they deep in their souls will think that the estimated
improvement
of say 20% (ci. (-5,+45)% ) is the TRUE effect. Eventhugh we can
persuade then to think otherwise.
And hence, as Hoenig and Heisey point out, essentially we are just
providing a determinsitic transformation of the p-value. And in vain
trying to convince clinicians that this is all there is to it while they
believe something important has been derived for them. And most likely
to the effect that there IS an effect of 20% we were not just good
enough to show it. It is important to maintain that there is no evidence
of effect, and that the ci. is the end of trial so to speak.
Best,
Bendix
> -----Original Message-----
> From: MedS...@googlegroups.com
> [mailto:MedS...@googlegroups.com] On Behalf Of John Whittington
> Sent: 19. november 2007 16:24
> To: MedS...@googlegroups.com
> Subject: {MEDSTATS} Re: retrospective power calculations
>
>
>I cannot help wondering what the average clinician would think of
>"what we know now" given an insignificant trial result.
>
>I bet that they deep in their souls will think that the estimated
>improvement
>of say 20% (ci. (-5,+45)% ) is the TRUE effect. Eventhugh we can
>persuade then to think otherwise.
>
>And hence, as Hoenig and Heisey point out, essentially we are just
>providing a determinsitic transformation of the p-value. And in vain
>trying to convince clinicians that this is all there is to it while they
>believe something important has been derived for them. And most likely
>to the effect that there IS an effect of 20% we were not just good
>enough to show it. It is important to maintain that there is no evidence
>of effect, and that the ci. is the end of trial so to speak.
I think there is probably somewhat of a misunderstanding here.
I hope we can all agree that the first thing to be done is to impress upon
the investigators that 'the result is the result' (i.e. 'no evidence of
effect'), and that no amount of waving of statistical 'magic wands' will
alter that.
I am talking about what happens after that. If a trial of adequate power
has produced 'no evidence of effect', then that will often mean that an
investigator (and, perhaps even more so, a trial sponsor) will not see any
need/merit in investigating the treatment (or whatever) any further. On
the other hand, if it can be shown that the study had proved to be
seriously under-powered, then there could well be a desire to conduct
further, adequately powered, trials.
Exactly, and that is why it is essentail to communicate the information
that data is also compatible with quite a high rate of side-effects. And
that this cannot be explained away by statistical mumbo-jumbo.
Bendix
>On Nov 19, 2:20 pm, kornbrot <d.e.kornb...@herts.ac.uk> wrote:
> > A priori power is always recommended to support determination of N, but
> depends on assumption about population SD.
> > Actual result may show an underestimate of SD. In this event, it is
> reasonable to give a post hoc power based on new SD estimate.
> > In such a situation it is INFORMATIVE to report: the magnitude of the
> difference was large, but due to large sample variability the power [post
> hoc] to detect an effect that would have large clinical significance was low.
Exactly - and that is the situation I've been discussing, and the
particular situation in which I've been 'defending' the concept of post-hoc
power calculations.
>I think the case being discussed would have a larger SD in the
>observed data than was used for the a priori sample size estimate,
>would it not?
I think that Diana and you are saying the same thing - i.e. that the SD
figure used for the a priori sample size estimation proved to be an
underestimate of the actual SD observed in the study.
>I think the key words there are "to detect an effect that would have
>large clinical significance". This sounds like a follow-up power
>analysis that uses a revised estimate of the SD (based on the observed
>data), but keeps the same measure of effect size as the a priori
>sample size estimate.
Indeed - and, as above, that's what I've been discussing and 'defending'.
>As I understand it, this is not what is typically meant by "post hoc"
>power analysis. I *think* that standard post hoc power analysis uses
>both the SD and the effect size measure from the observed data. And
>in that case, as Russell Lenth observes (in his "Two Bad Habits"
>article), observed power is just a transformation of the observed p-
>value.
Ah, if that interpretation of the terminology is correct, then I have not
been talking about 'post hoc power analysis'!! As Bruce, Lenth and many
others have observed, to calculate 'power' retrospectively on the basis of
the observed variability AND the observed effect size would seem to be just
plain silly - and, as they say, mathematically just another way of
presenting what is effectively a p-value from a hypothesis test or a
CI. Even if one forgets the mathematics, the whole concept of 'the power
to detect something that has already been observed' is more than a little
questionable - not that much different from looking for a 'probability'
that last week's lottery had a particular result!
>I can see some merit in doing a follow-up power analysis that uses a
>revised estimate of the SD. But using the observed effect size
>doesn't make a lot of sense to me.
That is certainly my poistion, and the one I've been trying to present.
>....Unless (I suppose) it has convinced you that you were previously wrong
>about how large an effect is practically important.
Yes, although it'[s a very dangerous slippery slope to get onto, the
results of a study may make one 'realise' that one's up-front specification
of 'how large an effect is practically important' was incorrect/unrealistic
- but if that were the case, one could engage in those thought processes
simply by looking at the observed effect size, without any need for any
'power calculations'. It also goes without saying that if one decides
retrospectively that the study should have been designed to detect a
smaller effect, that the required sample size would have been larger -
again, without any need to 'quantify' that with 'power calculations'. I
therefore do not think that those considerations really represent any
justification for the sort of 'post hoc power calculations' which we all
seem to agree are inappropriate.
As goes for the other ways of calculating (post-hoc) power it seems to
me that they aim a planning the size a future study based solely on
information from the current, which to me seems even more futile. There
is nothing wrong with calculations of power (or precision!) but I still
find it hard to understand why it is relevant to discuss future studies
as an integrated part of reporting one.
Best
Bendix Carstensen
> -----Original Message-----
> From: MedS...@googlegroups.com
> [mailto:MedS...@googlegroups.com] On Behalf Of John Whittington
> Sent: 20. november 2007 12:03
> To: MedS...@googlegroups.com
> Subject: {MEDSTATS} Re: retrospective power calculations
>
>
There was some debate on the SPSS list a few years ago about this, and
it turns out that post hoc power (of the kind using the estimates from
the data) isn't a transformation of the p-value in MANOVA (as in with
multiple outcome variables, to clarify, as MANOVA, like post hoc
power, can mean so many different things). I don't recall it made
the concept any more useful though.
[snip]
Jeremy
--
Jeremy Miles
Learning statistics blog: www.jeremymiles.co.uk/learningstats
Psychology Research Methods Wiki: www.researchmethodsinpsychology.com
>There was some debate on the SPSS list a few years ago about this, and
>it turns out that post hoc power (of the kind using the estimates from
>the data) isn't a transformation of the p-value in MANOVA (as in with
>multiple outcome variables, to clarify, as MANOVA, like post hoc
>power, can mean so many different things). I don't recall it made
>the concept any more useful though.
Well, yes, once one moves away from the simplest of hypothesis testing
situations, things get more complicated and hence a 'power calculation'
will not literally be a 'transformation of the p-value'. Apart from
anything else, 'a power calculation' is not itself a very straightforward
concept when there are multiple outcome variables. However, I think it
will always remain the case that 'a power calculation' performed using the
observed variability and effect size will be little more than a
manifestation of some (perhaps not the intended/appropriate) hypothesis
test on the data, and therefore neither appropriate nor useful. Indeed,
when the intended analysis is 'more complicated' (as in Jeremy's example),
I would have thought that the argument against that sort of power
calculation' would be even stronger (if that is possible!).