Conversation with Jon Pedersen on Iraq mortality studies
November 26th, 2006
I have posted the following comments on the Media Lens Message Board as part of a discussion of Jon Pedersen’s skepticism regaring the Lancet 2006 Iraq mortality figures.
I have had a number of emails with Jon Pedersen going back to last spring, if I remember correctly. I also had the privilege of having lunch with him and discussing these issues for almost a couple of hours.
He struck me as extremely thoughtful and as having no ax to grind. As I relate his thoughts, [I am responsible for this account, which could be incorrect on details. Comments in brackets are my thoughts.] he believes the Lancet rates are too high. He thinks two things are involved, and had two other comments on the methodology.
1. The prewar mortality is too low. This would be due to recall issues. He asserted that demographers are well aware that there are problems with assessing mortality by survey more than 1 year in the past. [See, for example, the SMART methodology which states that one should never assess mortality beyond one year: "Accuracy: The shorter the recall period, the more accurate the estimate of mortality. This is because more distant events are more likely to be forgotten by respondents and there are likely to be more mistakes in the time of death. (Recall periods longer than one year should not be used.)" (p. 31-32)]
[As a research psychologist, this is not surprising. We routinely find that memory, even for major events, gets transformed relatively quickly. As one minor example, one half of those who, at age 18 reported major depression did not report ever having had major depression ever, when reinterviewed at age 21. Especially in the context of a brief interview, it is entirely possible that people could briefly "forget" deaths a ways back, or "choose" not to talk about them as they may be painful. I, too, was concerned about this recall issue.] Pedersen said it was possible that this effect may be larger for nonviolent than for violent deaths.
[Note that, if the UN prewar mortality rate of 9.03 is correct, this will not, by itself, change the qualitative message of the study. My calculations are that the excess mortality would then be about 350,000. But other problems would arise, such as the mortality rates for the two years postwar, which would then be low. These might support the Pedersen/SMART position that 1 year prior is the outer limit for good results with this methodology.]
2. Pedersen thought that people were likely reporting nonviolent deaths as violent ones. [One argument for this is the surprisingly low postwar mortality rates in the Lancet 2006 study, which Pederesen thought were unlikely to be correct.] We did not discuss the precise mechanisms for this misreporting, or Pedersen’s other reasons for believing it.
[We did discuss the issue of the death certificates, to which Pedersen said "who knows what's on them." I have since found two accounts of death certificates which indicated that they have details of the death. More details from the Lancet authors as to the details of how and to what degree interviewers examined the certificates would be helpful.]
3.A third issue concerns the inability, because of security, of the US Lancet team to supervise the interviewers. Pedersen raised the possibility of his FAFO team repeating the survey, but was extremely hesitant as they would not be able to closely supervise the interviewers and,therefore, could not vouch for the protocol being followed exactly.
4. Pedersen believes the confidence intervals (CIs) for the Lancet studies are too small. This involves two issues. First, the calculated CIs only include sampling error, but the study also includes nonsampling error, as in when a different household was chosen for security reasons or the protocol wasn’t followed for other reasons. Recall issues and other forms of inaccurate reporting would also increase nonsampling bias.
A second reason the CIs are too small is a technical one. Death is a relatively rare event. The statistical methods used to calculate CIs [linearized variance estimators] are based on an assumption that the events aren’t too rare. Thus, the CIs are likely too small.
[While the Lancet 2006 authors say they also calculated bootstrap standard errors, they give no detail on how this is done, and are not clear which CIs they report. Bootstrap CIs with survey data are very complicated and can be done many different ways with, potentially, different results.]
Two additional points: Pedersen acknowledges that the ILCS cannot be the gold standard for mortality as asking one brief set of questions at the end of a long survey would lead to underreporting of mortality. Thus, he assumes that the ILCS figures are low. But he thinks they are in the ballpark.
Another point: He thinks that the IBC argument about how the number of bombings reported in the Lancet 2006 study would result in such a large number of wounded that it seems too large. If I understood correctly, he does not buy the IBC argument about the inconsistency between the estimated wounded and those reported as treated in hospitals, as he agreed [I thought] with a point I made that there were likely serious problems with Iraq’s health surveillance systems, so that these figures cannot be taken very seriously. But, he felt that 800,000 or more wounded would swamp any public heath system in the world. [An additional point occurred to be after the conversation. As one who has read the press on Iraq, including Iraqi bloggers, very carefully, I can't remember reading articles about the walking maimed of Iraq. It does seem that, if the Lancet mortality figures were correct, that the magnitude of wounded would be such as to be reported frequently.]
—————
I want to reiterate that Jon Pedersen, as far as I could tell, was extremely thoughtful. Several times he raised an argument only to raise a counterargument. He did NOT appear to be argumentative or to be involved in proving a point. I was extremely impressed. Therefore, I take his arguments and thoughts seriously. He may know more about middle east demography and survey methodology than anyone, so his judgments and intuitions cannot be simply dismissed.
I would also remind people that Les Roberts refers to Pedersen as “he highly revered Jon Pederson.” Pedersen also spoke highly of Roberts. These are scientific debates, and scientific debates do not always have bad guys. They also are often unresolvable with the current state of knowledge.
By the way, Pedersen did NOT think that there was anything to the “Main Street Bias” issue. He agreed, I thought, that, if there was a bias, it might be away from main streets [by picking streets which intersect with main streets]. In any case, he thought such a “bias”, if it had existed, would affect results only 10% or so.
As to his not communicating with Les Roberts, both he and I have sent emails to Les [I also sent one to Gilbert Burnham] which have not been responded to. There have been hundreds of emails on this issue, and people are very busy. Emails have been missed by many participants. Please cut out the snide comments about why people didn’t send emails to someone.
As to Pedersen’s writing a letter on this, I would hope he would. On the other hand, remember that he’s got a lot of other things going on. As far as I’m aware, he hasn’t sought out the role of critic but simply responded to those who asked his opinion. While such a communication would be very helpful, he is not obligated to undertake it.
So, the bottom line is that two experts differ. The rest of us are left trying to assess the differences. But we are also left not knowing.
That said, I’m not sure that the true mortality figure is as low as the 150,000 that Pedersen cites. I suspect the true figure is somehat higher, but below the 650,000 of Lancet 2006. But I can’t provide any strong arguments for my instincts here. I now take 150,000 that as the rock bottom number for Iraqi excess deaths. There may be more, even many more, but we can’t be sure. It simply is very difficult to get accurate figures in a time of chaos.
I would say that the moral case regarding the war is well made if the true excess mortality is “only” 150,000. This war and occupation has resulted in horrifying death and destruction. It is morally unjustifiable on any grounds of reducing harm.
Entry Filed under: Iraq,Middle East,Mortality,Public Health,Research Methods,Rights and Liberties,Science,Social Issues,War and Peace
15 Comments
1. Donald Johnson | November 30th, 2006 at 4:48 pm
Thanks for posting this. Joseph E pointed it out to me over at Deltoid.
What strikes me is that if Pedersen is admitting that the ILCS survey is low, but in the ballpark, then there probably isn’t a conflict between Lancet 1 and ILCS for the first 13 months. Lancet 1′s midrange estimate for violent deaths was about 60,000 for the first 18 months–for the period covered by ILCS it would be roughly 40,000 deaths. ILCS said 24,000 plus or minus about 5000 deaths for that period and this was “war-related” deaths, a vague category apparently excluding criminal murders, which were included in Lancet 1. So if ILCS undercounted violent deaths and may not have included criminal murders in its range, there’s no reason to claim, as Iraq Body Count did, that there is a conflict.
There is an apparent conflict for Lancet 2, which has between 50,000 and 130,000 violent deaths in the first 13 months if you use their 95 percent CI for violent mortality for that period. But the low number might conceivably be reconciliable with the ILCS survey.
Which leaves me thinking that Lancet 1′s midrange numbers were very reasonable. IBC has been using ILCS as its justification for claiming that they are picking up at least 50 percent of the violent deaths, but that argument falls apart if Pedersen admits that his survey probably gave an undercount.
2. admin | November 30th, 2006 at 7:11 pm
Donald,
Yes, I agree, if one assumes even a modest undercount in the ILCS, the difference between Lancet 2004 and ILCS is removed. Even more relevant is that the ILCS fieldwork in both Fallujah and the Shia south was completed before the fighting. that is, by early April. In Lancet 2004, something like half the non-Fallujah violent deaths were from April on.
IBC incorrectly used extrapolation on ILCS, when we know the fighting escalated in April. Further, Pederesen agreed with me that the ILCS could not be taken as a gold standard, since he admits an undercount. That said, he does think the undercount was not that high.
We should keep in mind, though, that ILCS included at least some military deaths during the invasion, which Lancet studies tried to avoid (with 2 month residency requirement). So some ILCS numbers are due to this, reducing the numbers comparable to Lancet.
I do think there is an incompatibility between Lancet 2004 & 2006 regarding the number of violent deaths (roughly a factor of 2) for that time interval. There is also a major incompatibility regarding the nonviolent deaths (app. 49% vs. 0% excess deaths)
3. Robert Chung | December 1st, 2006 at 5:04 am
Thanks for posting your interchange with Jon Pedersen. I have a couple of comments.
First, about recall bias: the SMART guidelines on recall period are designed to address estimating the level of crisis mortality, not estimating the change in pre/post mortality around some event in the past. Demographers often use survey recall periods much longer than a year when reconstructing both fertility and mortality histories, and are quite aware of recall bias. In general, the problem is worst with infant and child deaths, not with adults — and in the context of Iraq, most of the deaths being discussed in the Roberts and Burnham papers are not infant and child deaths. Certainly, it is often true that recall bias can manifest itself as “telescoping,” where the date of death gets misreported rather than the death itself being omitted, but I would think that seeing the actual death certificate would help to minimize and correct for this.
Second, the CIs reported in the Roberts and Burnham papers were bootstrap CIs, based on the cluster means.
4. admin | December 1st, 2006 at 8:01 am
Thanks Robert. Not being a demographer, I spent a day searching for sources on “mortality, survey, and memory” finding nothing. I should have thought of the term “recall bias”. BTW, do you have any sources on recall bias in mortality?
My concern, as a psychologist, is that memory can be very fallible, including non-recall of even major events, such as death. When we do longitudinal research, we find that memory for such things as the presence of major psychopathology degrades very rapidly after 6 months to a year. People do a lot to forget unpleasant events. Death certificates, of course, cannot correct for deaths that are unreported.
As for the CIs, I didn’t see the paper saying that they were bootstrap CIs. All I recall (don’t have it in front of me) is that it said both types of CIs were calculated. I couldn’t find where it said which were reported. In any case, in a recent email to me, Les Roberts said the two types of CIs were very similar.
I am not an expert in bootstrap methods. Jon, who knew more about it than I do, said that bootstrap variances (from which CIs are derived) are very tricky, especially in the case of complex sample surveys.
Thanks again.
5. Robert Shone | December 1st, 2006 at 10:54 am
Stephen, your description of Pedersen’s thoughts on “main street bias” is far from clear. You say Pedersen agreed there might be a bias “by picking streets which intersect with main streets”. If that’s the case, then it seems incorrect for you to assert that Pedersen “did NOT think that there was anything to the ‘Main Street Bias’ issue.”
Main street bias addresses precisely the fact that the Lancet methodology selected streets which intersected main streets. If Pedersen agrees there’s a potential bias here, then he seems by definition to be in agreement with the main street bias authors, contrary to your interpretation.
6. Robert Chung | December 1st, 2006 at 1:16 pm
Stephen:
Mortality estimation using survey instruments has a pretty long history, though it’s only been since perhaps the mid-1960′s that there have been systematic efforts to handle recall bias issues, probably spurred by the explosion in survey data collected from third world countries in that decade. Basically, this is the entire (sub-)field of indirect demographic estimation. Brass’ methods focused on infant and child mortality because they’re the biggest problem — infants who die are typically also more likely to be overlooked in reproductive histories so they are omitted both from the numerator and denominator of rates, and also because infant and child mortality tends to be high and variable. Adults are less often missed (which makes indirect estimation of adult mortality more reliable than for infants and children under five) though there definitely appear to be differentials across characteristics of the decedent and the survey respondent. For example, women tend to be missed more often than men; adult siblings tend to be poorer at recalling events than a parent is; and adult women appear to be better than adult men. That’s why the DHS surveys (demographic and health surveys done in many countries around the world) specify a ranking for preferred respondent.
I emphasize that I do not have any first-hand knowledge of how the JHU/AMU team collected their data, but well-done demographic surveys are designed to help minimize issues of recall bias, much in the way that you’ve described verbal prompting. For example, note that in these two studies, they didn’t just collect counts of deaths — they actually needed household histories in order to calculate person-months of exposure. Household histories are generally regarded as the best way to do this because they tend to have less recall bias. So you’re right, death certificates don’t correct for omissions; but household histories minimize omissions and then the DC can be used to hammer down the timing. As an aside, the ILCS/IMIRA questionnaire didn’t ask its mortality question in this way so there’s no “timing” in the reported deaths. Likewise, many crisis mortality studies don’t collect household histories this way, which is probably why the SMART guidelines are for short recall periods.
As for the bootstrap CIs, Pedersen was obviously talking about parametric CIs. In both the Roberts and Burnham papers, bootstrapping is mentioned at the bottom of (their respective) page 3. I sort of disagree that the bootstrap is tricky — it’s impressively simple-minded (though it took a very bright guy like Brad Efron to figure out something so simple). In any event, there is a big issue about whether it makes sense to bootstrap the cluster means, and how one gets from relative risk ratios to a point estimate of total excess deaths, but that isn’t strictly about the bootstrap procedure itself.
7. Robert Shone | December 4th, 2006 at 1:31 pm
Stephen Soldz wrote the following:
“By the way, Pedersen did NOT think that there was anything to the “Main Street Bias” issue…”.
I queried this with Jon Pedersen (who hadn’t read the main street bias material prior to his discussion with Stephen). He responded, in an email:
“Yes, probably Stephen Soldz confused the issue somewhat here. There are actual several issues:
1) I very much agree with the MSB-team that there is some main stream bias, and that this is certainly an important problem for many surveys – not only the Iraq Lancet one.
2) I am unsure about how large that problem is in the Iraq case – I find it difficult to separate that problem from a number of other problems in the study. A main street bias of the scale that we are talking about here, is very, very large, and I do not think that it can be the sole culprit.
3) The MSB people have come up with some intriguing analysis of these issues.”
(Jon Pedersen, email to me, 4/12/06)
8. joshd | December 6th, 2006 at 5:12 am
I see a lot of claims about IBC being wrong about this and that, based on what Pedersen has supposedly said to Soldz (Pedersen has already said Soldz didn’t get his views on MSB quite right). I think both of you guys (Stephen and Donald) are far too eager to find fault with IBC, and this is clouding your thinking.
First, Donald says:
“So if ILCS undercounted violent deaths and may not have included criminal murders in its range, there’s no reason to claim, as Iraq Body Count did, that there is a conflict.”
First, if any such undercount exists (again I don’t take Soldz’ version as being exactly what Pedersen has said – I suspect Pedersen was less certain about this than in Soldz version) he believes it is small.
Second, IBC already did remove all crime deaths from Lancet before the comparison. The comparison IBC did gave every benefit – undue benefit even – to convergence with Lancet:
1. We did not account for any combatants in ILCS that would be excluded from Lancet (even though Lancet says it would have excluded most military deaths during the invasion – as Stephen does acknowledge in his post above).
2. We did not account for the fact that Lancet subtracted 3,000 violent deaths in the “excess” calculation while ILCS used no such ‘excess’ calculation to subtract pre-war deaths.
3. We did not account for the fact that Lancet excluded Fallujah (which they say represents all of Anbar province). We compared Lancet’s estimate for 97% of Iraq to the ILCS’ estimate for 100% of Iraq. To be truly consistent we should have removed all of the Anbar deaths from ILCS before the comparison. We did not do this either.
All of these would drive the two much further apart than they already are in our comparison. A small underestimate of the kind Pedersen has spoken of would not change things much. And Pedersen saw and approved what we were writing about ILCS before we published it.
Furthermore, Roberts has long emphatically claimed that L1′s non-Falluja estimate is an “extremely conservative” underestimate, and he never ever has claimed that it would likely be only small. So if we are supposed to account for what the authors have conjectured about underestimation in their estimates, this would only, yet again, spread the two much further apart from each other. It would not bring them closer together.
Donald also says:
“IBC has been using ILCS as its justification for claiming that they are picking up at least 50 percent of the violent deaths, but that argument falls apart if Pedersen admits that his survey probably gave an undercount.”
This is also false. So eager to find fault with IBC. Again, Pedersen saw and approved our comparison with ILCS before we published it. He has known all along exactly what we’ve been saying about it. And IBC’s comparison of itself again took a very conservative path and gave every benefit of the doubt against itself. For example, it assumed only 3,000 combatant deaths even including Saddam’s military during the invasion, and assumed that absolutely 0 crime deaths were recorded as war-related deaths by ILCS, removing 100% of these from IBC before the comparison. Both of these assumptions almost certainly understate IBC’s coverage relative to ILCS.
Stephen says:
“Even more relevant is that the ILCS fieldwork in both Fallujah and the Shia south was completed before the fighting. that is, by early April 2004″
Where did you get this from Stephen? ILCS had hundreds of surveyors working up to May 25th. And there is no increase in April 2004 in L1. April is *lower* than March in L1. Only in Falluja is there an April increase. And as I said above, in a truly consistent comparison between ILCS and L1, Falluja should be removed altogether from ILCS just as it was removed from L1.
And I have no idea what you think you’re referring to with “before the fighting” in April 2004 in the Shia south.
One of the things the pro-Lancet crowd has persistently done is spuriously downsize the ILCS timeframe to favor Lancet. Lambert has regularly taken the line that ILCS covered “13 months”, assuming 0% coverage of deaths in May, even as they were surveying up to May 25 2004 (over 14 months after the start of the invasion). That recent piece by Iraqanalysis.org even more ridiculously chopped this down further to “12 months”, excluding all of April and May. There is some leeway here, but the timeframe is neither 13 nor 12 months. It’s somewhere over 13 months but probably somewhat less than a full 14 months.
“In Lancet 2004, something like half the non-Fallujah violent deaths were from April on.”
That’s incorrect too. It’s nowhere near half. Only in the Fallujah cluster is April unusually high. And only July is particularly high in the post-April months outside Falluja. August is very low, and September is low.
“IBC incorrectly used extrapolation on ILCS, when we know the fighting escalated in April.”
Nonsense. Fighting escalated in Falluja in April. But as I said above, Falluja shouldn’t even be included at all in ILCS if we’re doing a comparison to an L1 estimate that is excluding Falluja/Anbar.
Furthermore, IBC applied Lancet 2004′s timeline, so it is increased proportional to Lancet data. Any post-April increase in L2004 would be reflected in our correction of ILCS.
And the same conclusions follow when you don’t do the “extrapolation on ILCS” and go the other way, removing the post ILCS deaths from Lancet:
http://scienceblogs.com/deltoid/2006/04/ibc_takes_on_the_lancet_study.php#comment-82524
No matter how you slice it, the two don’t line up. Regardless, Roberts has recently taken to calling the ILCS a “gross underestimate of deaths”, so I think they’ve abandoned any care about themselves lining up with ILCS.
9. admin | December 6th, 2006 at 4:29 pm
Josh, you’re partly right. My statement
is incorrect, or at least an exaggeration. (This is the problem of writing from memory.) First, I do agree that the non-Fallujah comparison is the correct one, and is the one I intended. If my count on their Figure 2 is accurate (my eyes are old enough that I can’t quite see the red), 13 deaths occurred in the 13 months from March 2003 to March 2004 while 8 deaths occurred in the 6 months from April 2004 through September 2004. 8 is under half, though it is at a somewhat elevated rate, which is what I must have remembered.
As to where I got my statement
My source is, of course, Jon Pedersen. Here is an excerpt from an email from him on May 2 2006. My question in NOT bolded, his response is:
And here is an exchange from an email of May 3 2006:
With regard to the question of ILCS estimates being low, here is an exchange from an October 26 2006 email:
With regard to Robert (“Bob”) Shone’s comment in which Pedersen says I may have gotten his position wrong on the Main Street Bias, this is entirely possible, as I was relying upon memory and we had only limited time to discuss. I actually think my summary of his position (Robert, did you ask his opinion on my entire paragraph on the issue, or only on the phrase you extracted, which is taken out of context.) is generally consistent with what he said in the email to Shone.
I had not intended to imply that Pedersen didn’t think the Main Street Bias issue was a possible issue for surveys, as we didn’t discuss that. We only discussed whether it could explain the discrepancy between L2006 and the mortality figure that Pedersen believes is correct. The 10% figure came from him spontaneously. He may since have increased his estimate.
In any case, here was his November 28 response to reading my account of his thinking:
He doesn’t seem to feel he was grossly misrepresented, as Josh, and, perhaps, Robert S. are suggesting.
10. joshd | December 6th, 2006 at 6:13 pm
“He doesn’t seem to feel he was grossly misrepresented, as Josh, and, perhaps, Robert S. are suggesting”
Thanks for posting this Stephen. I’d point out however, that i did not say or suggest that you “grossly misrepresented” anything. What I was saying was that nuances can be lost or get twisted around when one person is describing a complicated discussion with someone else from memory. As such, I don’t take the exact phrasings you chose to use as if these were direct quotes of Pedersen, as some others have done. That is all.
11. admin | December 7th, 2006 at 8:49 am
Thanks Josh,
I cannot interpret your statement
as making a claim slightly stronger than one of “nuance.”
I agree totally that nuances can be distorted. That was why, in my original account, I placed lots of hedge words, such as “I think,” to indicate that it was my version. However, I also took the precaution of sending the comments to Jon to give him the opportunity to correct me, if he so chose.
I do wonder if Pedersen was reminded by Shone of my entire statement on MSB when he was solicited to comment on it. Again, a matter of nuance. [I put this to Robert Shone, but, suddenly, after sending me several emails a day, he became "too busy" to respond to my simple inquiry.]
12. Robert Shone | December 7th, 2006 at 9:41 am
Stephen, you write that you “had not intended to imply that Pedersen didn’t think the Main Street Bias issue was a possible issue for surveys”. If you didn’t intend to “imply” such a thing, then why did you so emphatically state it: “Pedersen did NOT think that there was anything to the ‘Main Street Bias’ issue.” [Your uppercase emphasis; my bold]
Nothing else that you wrote in your above article mitigates this overstatement (and I think “overstatement” is putting it charitably). You should know that such statements are quickly quoted across the web (Tim Lambert wasted no time quoting you on Deltoid, for instance).
Your last sentence is hypothetical (and therefore irrelevant to your earlier assertion): “In any case, he thought such a “bias”, if it had existed, would affect results only 10% or so.” [my bold]
Stephen Soldz wrote:“Robert, did you ask his opinion on my entire paragraph on the issue, or only on the phrase you extracted, which is taken out of context.”
Stephen, I didn’t “extract” anything “out of context”. My email to Jon Pedersen (as well as providing a link to your piece), included both your emphatic statement:
“Pedersen did NOT think that there was anything to the ‘Main Street Bias’ issue.”
And also your statement immediately following it:
“[Pedersen] agreed, I thought, that, if there was a bias, it might be away from main streets [by picking streets which intersect with main streets].”
My query was specifically about the contradiction between the above two statements (“Given that the MSB criticism in fact addresses precisely the bias resulting from selection of streets *intersecting* main streets, the above two attributions of your views from Soldz seem contradictory.”)
If you were unsure either of what Pedersen was saying, or of what main street bias says, then perhaps you shouldn’t have been so emphatic in saying that Pedersen “did NOT” think there was “anything” to the main street bias “issue”.
13. Robert Shone | December 7th, 2006 at 10:18 am
Stephen Soldz wrote:
[I put this to Robert Shone, but, suddenly, after sending
me several emails a day, he became “too busy” to respond to my simple inquiry.]
Stephen, I think you’re one of the more moderate and intelligent commentators on these issues, and I appreciate your taking the time to discuss them with me. But I must take issue with the above.
I’ve received four emails from Stephen during a correspondence I initiated (in which I sent a total four emails in reply to Stephen’s four – plus one postscript containing a link to an article I thought he might find useful).
As for my “too busy” comment, it was in response to an email from Stephen which raised many issues, including “extreme assumptions” in the MSB work, instability over time of variables which affect whether a given area is a “safe zone” or a “danger zone”, the above reference to whether I quoted him in full to Pedersen, his (Soldz’s) agreement on the importance of revealing errors in L2, his reasoning on why he thinks IBC are “wrong” on various points, several other points concerning IBC, and other points concerning questions over L2 etc.
It was to all the above that I had no time to respond in full, as I was “too busy” (but I did say I would respond in a few days time – I sent that on 5/12/06). And now I’ve responded in full (at least to the Pedersen email thing), as promised, a few days later.
14. Psyche, Science, and Soci&hellip | December 11th, 2006 at 2:09 pm
[...] Of course, the fact that the mortality rates are not implausible does not mean that they are therefore correct. While many epidemiologists and others have defended the study, some experts in this area, most notably the eminent Norwegian researcher Jon Pedersen have criticized the study. Like all studies on important matters, this one does deserve careful scrutiny. But it does not deserve to be dismissed by the press in a way that similar studies with results more comfortable to the United States government are not dismissed. The existence of “controversy” should not be an excuse to ignore that, as a consequence of U.S. government action, hundreds of thousands of Iraqis have needlessly died. [...]
15. Psyche, Science, and Soci&hellip | March 1st, 2007 at 8:42 am
[...] Ultimately, as Burnhmam said when he spoke at MIT Tuesday, the answer is unknowable. Science advances by replication. In this case, I’m not sure that replication is possible. Personally, I would like to see a collaboration between the Lancet study team and Jon Pedersen, the director of the Iraq Living Conditions Survey, the only other epidemiologic survey to attempt to assess Iraqi postwar mortality. Having met and corresponded with all three of Jon Pedersen, Les Roberts and Gilbert Burnham, I have great respect for all three. Science in difficult conditions has sometimes advanced through collaboration of those with differing perspectives, or even “biases.” That way, they can control for any potential unconscious “bias.” [I rule out deliberate bias in this case.] Jon’s extensive experience conducting surveys in the Middle East could compliment Les and Gilbert’s experience with assessing mortality in conflict situations. Personally, I would love to be in on their discussions designing such a study! This subject would be a natural, should the conditions in Iraq ever be safe enough to allow further mortality studies. [...]