A paper of mine was published in the open-access Electronic Journal of Statistics. It proposes a method of constructing lower confidence bounds for positive random variables that are guaranteed to have the nominal coverage probability for any distribution, as long as the sample points are i.i.d., from a distribution over the non-negative reals.

In the paper, the method is applied to analyze (a version of) the data of the second Lancet study of mortality in post-invasion Iraq.


ORB vs. IFHS in U.S. Media

February 1, 2008

On January 28th, the British polling firm Opinion Research Business (ORB) released an update (via Deltoid) of their previous study estimating violent deaths in post invasion Iraq. The update claims to confirm the previous findings, that about one million Iraqis have died violently following the U.S.-British invasion.

Today, about 3 days later, there are 91 hits on Google News for the combination “opinion research business”+iraq (counting duplicates). The one major mainstream U.S. outlet among the 91 is Reuters. At the same time, searching for articles covering the three weeks old release of the IFHS study shows 295 hits (using the combination iraq+”new england journal of medicine”+151000 OR 150000, and counting duplicates), with all the major mainstream U.S. new outlets represented (The New York Times, CNN, The Washington Post, CBS, USA Today).

Another matter: There is much of interest in the ORB study. Detailed tables give various breakdown statistics: 17% of households surveyed experienced at least one violent death; in Baghdad, that proportion is 36%; of the violent deaths 40% were by gunshot. It would be interesting to compare (in a different post) some of the data to what is available in the IFHS.

The main discrepancy between findings in the IFHS paper and those of Burnham et al. is not in the total excess deaths, but in the specific category “violent deaths”. It is therefore of interest to examine whether the classification methods used in those papers to assign deaths to the “violent” category are identical, and whether any differences in the classifications could account for some of the different findings. I notice two points on which the papers’ methodologies of classification differ: One is that Burnham et al. examined death certificates, while IFHS did not. A second difference is that they use different categories for injuries. Burnham et al. use two “accident” categories. One of those is included in the “non-violent” section, the other in the “violent” section. IFHS has no “violent accident” category, and has two categories, “road accidents” and “unintentional injuries”, counting injuries within the “non-violent” classification.

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Justifying the factor used to account for under-reporting of deaths

The IFHS sample is a very low mortality group. For the pre-invasion period of about 1.25 years, the group, which contains 61,636 individuals, experienced 204 deaths. For post-invasion period (about 3.25 years) , the group experienced 1,121 deaths. These translate to 2.65 deaths per 1000 person-years, and 5.6 deaths per 1000 person-years, respectively.

The IFHS sample was not designed to be equal weight to begin with (i.e., some people had higher chance of being selected than others), and biases certainly increased after some clusters were dropped from the sample because they were considered too dangerous to access. Re-weighting (in some way – it is not clear whether the adjustment procedure for total mortality is the same one as that used for violent deaths) by the IFHS authors yields significantly higher mortality rate for the pre-invasion period: 3.17 deaths per 1000 person-years (95% CI 2.70–3.75), and somewhat higher rate for post-invasion period: 6.01 deaths per 1000 person-years (95% CI 5.49–6.60).

The low mortality rate is probably due to a certain extent to a young population – I was unable to find the breakdown of the sample by age (neither in the IFHS paper, nor in the report). The mortality rate is much lower, however, than that of the sample of Burnham et al. – not only for the post-invasion period but also for the pre-invasion period. Burnham et al. estimated the pre-invasion mortality as 5·5 deaths per 1000 person-years (95% CI 4·3–7·1). Thus the fact that IFHS authors find it necessary to adjust their estimate upward seems justified.

The problem is, however, to find the appropriate adjustment factor, and to account for any uncertainty in that factor. The authors mention (p. 486), with reservation, the figure of 62% as the proportion of deaths being reported (i.e., 38% go unreported). They also mention (p. 487) modeling the proportion going unreported as being a normal variable with mean 35% and “95% uncertainty range, 20 to 50”, which I take to mean that the standard deviation is (50-35) / 1.96 =~ 7.5%. The ratio between the Burnham et al. and IFHS point estimates for the war mortality rate is 5.5 / 3.17 = 1.74, which would stand for 42% of the deaths going unreported.

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An explanation of the concept of effective sample size is here. This post applies this concept to a particular study.

Extrapolating from a sample taken in a reference area containing a relatively small number of deaths in order to estimate the number of deaths in the area containing the bulk of the deaths in Iraq is problematic even if we assume that the extrapolation factor is known precisely.

The reference area is the “three provinces that contributed more than 4% each to the total number of deaths reported for the period from March 2003 through June 2006″. By the design of the sample, there are no more than 180 clusters in these provinces (each province was sample with 54 clusters, except for Nineveh which was sample with 72 clusters). Table 3 of the supplementary material of the paper shows that sample sizes in each governorate. Taking the largest 3 samples in the “High mortality governorates” section (Nineveh, Babylon and Basra) gives an upper bound on the total sample in the reference area of 14,891 people. Multiplying that bound with the mortality rate in the area (Table 2 of the supplementary material) – 0.83 death per 1000 person-years – gives an upper bound for the number of violent deaths in the sample in the reference area of 14,891 x 0.83 / 1000 x 3.33 = 41.19.

That is, over 70% of the deaths in the IFHS estimate – those in Baghdad, Anbar and the three reference governorates – are based on a sample containing about 40 deaths. The estimate of the number of deaths in those areas is generated simply by multiplying those 40 deaths by a factor and thus any uncertainty in the number 40 is directly translated into uncertainty in the estimator of the total number of deaths in the areas.

Reference to the large total number of clusters in the IFHS (almost 1000 clusters visited) is therefore misleading. The determining factor of the estimate is the data collected in a much smaller number of clusters – generating a small number of recorded deaths. The uncertainty in the estimate is correspondingly large.

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Missing clusters

The IFHS surveyors did not visit all of the clusters in their sample. Those areas that were judged to be dangerous went unsurveyed. Most of the unsurveyed clusters were in Baghdad (31 out of 96) and in Anbar governorate (71 out of 108). A smaller number of clusters went unsurveyed in Nineveh (12 out of 72) and in Wasit (1 out of 54).

It appears that the missing clusters in Nineveh and Wasit were ignored. This has the potential of introducing significant bias into the estimate of mortality in those governorates. Removing the clusters in areas within a governorate that were considered dangerous turns the estimator into an estimator of the non-dangerous areas. It seems likely that the mortality in the non-dangerous areas only would be smaller than in the governorate as a whole. If the dangerous areas had seen a significant part of the deaths in the governorate, then removing them from the sample would bias the estimator significantly downward, and the more dangerous a governorate is, the more significant the bias is.

Indeed, as can be expected from such a differential bias, the death rates in the various governorates in the IFHS sample (before any adjustments) show reduced variation compared to the death rates in the two sources that the IFHS authors compare themselves to – Burnham et al. and Iraq Body Count (IBC).

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According to the description of the sampling method of IFHS (both in the paper itself and in the supplementary material), 10 households were surveyed in each cluster, and there were (with few exceptions) 3 x 18 = 54 clusters per governorate. In such a set-up there should be no correlation between the number of people surveyed in each governorate and the size of the population in the governorate.

The chart below was generated using the data in table 2 of the supplementary material of the paper. Each of the 18 point corresponds to a governorate. The x-axis value is the population size in the governorate (calculated as the mean of the 5 values, for 5 different time points, given in the table). The y-axis value is the average sample per cluster in the governorate. The total sample size given in the table was divided by the actual number of clusters visited (54 for most, 65 for Baghdad, 60 for Nineveh, 37 for Al-Anbar and 53 for Wasit). A strong correlation between the two is evident. The correlation factor is 0.94. After removing the two outliers – Baghdad and Nineveh – the correlation factor is 0.72 (p-value 3×10^-5).

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Assuming that the description of the sampling method is correct, then it seems that the only way such a correlation could show up is if the size of the population in the a governorate is strongly correlated with the average household size in the the governorate. This is possible but seems unlikely a-priori. Another surprising finding in such a case would be the sheer range of household size variation – ranging from less 3.2 people per household in 3 of the smallest governorates to almost 20 people per household in Baghdad.

The possibility that the description of the sampling method is incorrect presents itself strongly.

Reviewing the IFHS study, I found 5 problems with the science of the study. I believe that taken together (but particularly the first three points, regarding the crucial role extrapolation plays in arriving at the estimates in the study, and regarding the ratio of under-reporting) those problems should be seen as grave. At the very least, they should be seen as putting the findings of the IFHS on equal or inferior footing to those of Burnham et al., rather than as being on superior footing due to the nominal large size of the sample in the IFHS.

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The IFHS study

January 17, 2008

The recent release of the IFHS study (via Deltoid) which put the number of Iraqis killed violently during the first 3 years and 4 months after the invasion at a mere 150,000 has generated the expected sigh of relief in the media (e.g., 1, 2, 3). Having previously been implicitly blamed for supporting an endeavor that generated 4 times as many violent deaths over the same period (Burnham et al., a.k.a. the second Lancet study), this new figure is celebrated as vindication.

Going over the pattern of media response to the IFHS study would be informative, but would produce unsurprising results. I therefore touch on only one point which also bears on the issue of any anti-IFHS bias by “Lancet supporters”.

Conveniently, the reports ignore the question of how many Iraqis died non-violently following the invasion as a result of the widespread devastation and breakdown of organization. This was helped to a large extent by the fact that the study itself, while giving an estimate for violent deaths, does not give an estimate for excess mortality – it merely gives pre-war and post-war mortality rate estimates. It is, however, quite easy to use those mortality rate estimates to generate an estimate for the excess mortality. Using those figures and applying the method used in the study to account for under-reporting, the estimate of excess deaths during the first 40 months after the invasion comes to around 400,000. This is not significant disagreement with the different from the Lancet figure.

The major disagreement between these two studies, therefore, is about what is the proportion of excess deaths were violent, rather than how many Iraqis died as a result of the invasion. The IFHS has it that only about 1/3 of the excess deaths are caused by violence – Burnham et al. put that figure at about 90%. In this disagreement, based on a-priori considerations, it seems that the IFHS findings are more reasonable. It would be a miracle if in a country of 30 million, there could be enough violence to cause hundreds of thousands of violent deaths, and yet non-violent mortality would barely budge.

In my mind, it is the total number of excess deaths that is of interest when trying to decide what is the cost in lives that is attributable to the invasion. It makes little difference to an Iraqi whether his child died when she was hit a bullet or when she was poisoned by contaminated drinking water. I also expressed the view that the ratio 10:1 violent to non-violent deaths estimated by Burnham et al. is problematic long before the IFHS was published.

I thus see no need to bash the IFHS study. It is however quite interesting to find that when examining the IFHS in a little detail (and it is really no more than a cursory examination that I undertook) several significant problematic points manifest themselves – I will enumerate them in an upcoming post (here). The fact that such problems exist is interesting for several reasons:

  1. The immediate interest is regarding the validity of the findings in the context of assessing the reality in Iraq and the impact of the decision to invade it.
  2. A second point of interest is the matter of how points of weakness are handled by various players (especially, powerful players, such as corporate media and the government). When do such points of weakness get to be played up and seen as undermining the credibility of a study and when do they get to be ignored or played down as mere nitpicking.
  3. An additional point is the fact that papers with such obvious weaknesses can pass the vaunted peer-review barrier – what does this imply about the process of peer-review and the politics of science?
  4. Finally, the broad epistemological issue – what can we know about what happens in other places? What do accounts, including scientific, establishment sanctioned accounts, teach us?

While I have been contemplating filling a much needed void in the blogosphere with my own humble contribution, the immediate trigger for this blog is a set of threads in Tim Lambert’s blog, Deltoid: 1, 2, 3.

Those three threads discuss a paper by David Kane, in which he purports to prove that there is a mathematical contradiction in the 2004 paper by Roberts et al. in the Lancet discussing mortality in Iraq before and after the 2003 US-British invasion.

There are apparently a few scientists among the readers and the commenters of Deltoid, and they proceeded to address Kane’s paper. Most of the commenters consider Roberts et al. credible and were critical of Kane’s paper. Kane’s paper is weak on its substance (namely, Kane thinks that having a sample point with very high mortality – Fallujah – indicates that the mean mortality may be very low), and so it is only natural to try to address this weakness.

The problem is that Kane had what he presented as a mathematical argument proving his point, so he could claim that what seemed to his critics as a weakness of substance is nothing but a failure of their own intuition. In his first few responses in the comments he would even claim that his critics’ position is equivalent to stating that 2+2=5.

However, Kane’s mathematics are even weaker than his substance. This may seem surprising, since his substance seems to be wholly without merit. However, while his substantantive claim makes grammatical sense, his math does not – it is a complete mess. His entire mathematical argument is jibberish.

My attempts to make this point (commenting under the name “Sortition”), stating exactly why he does not make sense, never got any substantive responses from Kane. He was apparently honestly mistaken and truly believed that his arguements were correct. It seems that he gradually began to understand that his thinking may be not quite rigorous, but was unwilling to follow through and withdraw his paper and retract his conclusions until further consideration of his arguments.

This was only to be expected. Kane is ideologically committed to his conclusions, and has a personal stake to boot.

The more surprising thing was that I found it hard to get any attention from commenters who were critical of Kane. They were apparently as unaware as Kane was that Kane’s mathematical argument was entirely false, and my claims that it was were not considered credible. In my frustration, I wrote to Tim Lambert, making my point in an e-mail, and suggested that a professional statistician could make a valuable contribution to the issue. I got no response.

This called for radical action – and Pro Bono Statistics is the outcome.

In the following posts I hope to deal with many issues. One would be to point, once again, where Kane goes terribly wrong. More generally I intend to deal with statistics, as a theory, and as applied to real world issues. Even more generally, I intend to deal with other things that I think need dealing with but are not being dealt with satisfactorily, either in the mass media, or in blogs.