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The most important benefits of screening healthy women, advertised officially for decades, were less invasive treatments due to earlier detection, better chance for recovery and, directly related to it, reduction in breast cancer mortality (BCM). Higher detection sensitivity, as shown on the previous page, turned into a negative: screened population consistently scores more diagnoses - due to diagnosing pseudo-cancers as real - and undergoes more treatment.

As for the better chance for recovery, it should have its final proof in the significantly reduced BCM rate. Does it?

Typically, BCM reduction figure used in promoting screening of healthy women was taken from those trials that have come up with the largest mortality reduction. Seems as if no one wanted to pay attention to the obvious contradiction. Those very trials had:

▪ the longest interval between screening (Two-County trial),

▪ had no more than 2-3 screenings for the majority of women (Two-County and Stockholm trials),

▪ started systematic screening of the women in the control group in as little as 3-5 years after beginning (Two-County, Göteborg, Stockholm), or

▪ had lower-quality mammography equipment (New York, where only 15% of breast cancers in the screened group was detected by mammography alone, which also did not detect a single cancer smaller than 1cm).

More importantly, a closer scrutiny of how large screening mammography trials were designed and executed revealed that those reporting significant BC mortality reduction benefit had serious quality issues - so much so that their results cannot be considered reliable.

Following table summarizes quality assessment of all randomized controlled trials that qualify for this particular subject matter, together with reported BC mortality in the screened vs. control population. In all, eight trials were analyzed (with the data provided for one that was excluded for unacceptable randomization bias), with a total of 600,000 participants. Raw data are given in the table below.
 

Vital statistics	TRIAL   ∎adequate   ∎inadequate   ∎flawed
	Age trial	Canada	Edinburgh	Göteborg	Malmö	New York	Stockholm	Two county
Screened Group BC deaths	53,884 105	44,925 212	28,628 176	21,650 88	20,695 87	31,000 218	40,318 66	77,080 261
Controls Group BC deaths	106,956 251	44.908 213	26,015 187	29,961 162	20,783 108	31,000 262	19,943 45	55,985 277

Numbers are taken from the systematic (i.e. including all eligible trials on this particular outcome) review by researchers from the Nordic Cochrane center (Screening for breast cancer with mammography, Gøtzsche and Nielsen, 2001/2009/2011). There were several other systematic reviews of the trials on screening mammography and breast cancer mortality, but they typically did not assess trial quality, or were limited to the certain age groups.

In general, numbers reported by these trials are used in all of these reviews; the interesting part is how reliable are the sources of these numbers. Here's the summary.

MAMMOGRAPHY SCREENING TRIALS: EFFECT ON BC MORTALITY
(Based on: Nordic Cochrane Center systematic review 2009)
∎ Adequate (A)  ∎ Unclear/Inadequate (B/C)  ∎ Flawed (excluded)
 

#	Trial	Age	BC deaths, screened vs. controls	CRITERIA				Class
				Proper randomization	No significant unbalanced exclusions	No early systematic screening of controls	Reliable cause-of-death assessment	A ∎	B ∎	C ∎
1	New York 1963	50+	0.78	?	X1	√	X2		∎
		50-	0.78
		All	0.83
2	Malmö 1976	50+	0.86	√	?3	√	?	∎
		50-	0.52
		All	0.81*
3	Two-Countya 1977	50+	0.64	?	X	X4	X5			∎
		50-	0.91
		All	0.68
4	Edinburgh 1978	50+	0.88	X6	X	√	X			∎
		50-	0.79
		All	0.86
5	Canadab 1980	50+	1.02	√	√	√	√	∎
		50-	0.97
		All	0.995
6	Stockholm 1981	50+	0.64	X	?	X	X		∎
		50-	0.96
		All	0.73
7	Göteborg 1982a	50+	0.83	?	?	X	X		∎
		50-	0.70
		All	0.75
8	Age Trial 1991	50+	n/a	√	√	√	?7	∎
		50-	0.83
		All	0.83
4 INADEQUATE TRIALS ∎		50+	0.70	CRITERIA BRIEF: ∙ Proper randomization should ensure that the risk is evenly distributed between screened and control group ∙ Significantly imbalanced exclusions from screened vs. control group during or after trial indicate possible bias or substandard randomization ∙ Early systematic screening of the control group (contamination) reduces the effect of intervention (i.e. contrast between groups) making the results less reliable due to insufficient trial duration ∙ Cause-of-death assessment blinded to group status is the basic - although not necessarily sufficient - requirement for reliable, unbiased classification of deaths in trial population
		50-	0.80
		All	0.75
3 ADEQUATE TRIALS ∎		50+	0.94
		50-	0.87
		All	0.90
ALL 7 TRIALS ∎∎		50+	0.77
		50-	0.84
		All	0.81
ALL-CANCER MORTALITY		∎	1.02
		∎∎	0.99
ALL-CAUSE MORTALITY		∎	0.99
		∎∎	0.99
*Pooled ratios are weighted  aKopparberg and Östergötland trials;  bCanada 1 and 2    1 Estimated 853 women excluded from the screened vs. 336 from control group 2 Case-of-death assessment unblinded to group status for 72% of women 3 137 women from the baseline screened group and 26 from controls missing from later records   4 Control group screening started within 3-5y 5 Case-of-death assessment not blind to group status 6 Nearly twice as many women with highest socioeconomic status in the screened group 7 No information on autopsy rate; no independent cause-of-death assessment

What the inspection of trial data showed is that the lack of transparency or documentation (?) and/or documented sub-standard features in the design and execution (X) were rather common in these trials. Comments added at the bottom are only a small portion of inadequacies plaguing most of them, given to illustrate their nature and extent. 

How confident can we be of these studies reporting on the effect of screening on breast cancer mortality, with the "Reliable cause-of-death assessment" column having

a single clear O.K. mark?

A trial with the iconic status in pro-screening arguments was - and still is - the Swedish Two-County trial, the most likely reasons being that it reported the largest BC mortality reduction of all, and that it had the largest number of participants. Never mind that it only used a single-view mammography, with most of the screened women having no more than three mammograms altogether, and that its control group was subjected to screening within 3-5 years from the start.

Never mind that this flies in face of the general consensus that for the screening-related BC mortality reduction to start showing requires at least 5-year period, and up to several years more to reach its actual higher level (a pattern consistently documented in all other trials is that

BC mortality is actually higher in the screened group for at least first few years).

Never mind that a meta study of the Swedish trials found that the Two-County trial evidence disagrees with the Swedish official cause-of-death register in that it reported 10 BC deaths fewer in the screened group, and 27 more deaths in the controls (Nystrom 2002, to which Holmberg et al. - including lead trial author for the Two County L. Tabár - responded in 2009, "explaining" the discrepancy by a different cause-of-death criteria applied, and entirely ignoring the main point, that the sum of death cause re-classifications in the trial was in favor of screening in both, screened and control group).

Or that other studies found that the Two County trial's BC mortality reduction figures agree poorly with the reported cancer stages for the two groups (Zahl 2001), and that a large number of breast cancer cases and deaths in the official register seem to be missing from the trial data (Zahl 2006).

Or that the specifics of trial's randomization process haven't been published yet, despite it's been well over two decades since it ended. Its trial randomization is suspect, among other reasons, for its two joined sub-trials, in Kopparberg and Östergötland, reporting BC mortality rate in their respective control groups that

differs nearly by a factor of two

(0.21 vs. 0.12%, respectively). Or...

Chances are, this trial avoided exclusion so far only due to its iconic status used by the mighty proponents of screening mammography for its popularization; but it could be only a matter of time.

These serious inadequacies are in stark contrast with the characterization of Swedish mammography trials - and particularly the Two County - as the most reliable by the pro-screening side. And no less with its dismissal of the only trial that found no BCM reduction with screening at all - the Canadian trial - which is unquestionably of the superior quality in both design and execution. One of the many objections thrown at it was that women in the control group in the Canada-1 trial (40-49y of age)

were thought to perform breast self-examination.

That, according to the critics, resulted in the control and screening groups being not comparable anymore (that despite the critics at the same time generally maintaining that breast self-examination has no appreciable effect on BC mortality).

But those same critics apparently have no objections to the fact that screened women in the Two-County trial were encouraged to perform monthly self examination.

Summing it up, the number of trials that we can use with a reasonable confidence to look for indication of the effectiveness of screening on BC mortality reduction, shrinks to three. Their combined reduction rate for the screened populations is statistically insignificant (i.e. indistinguishable from variations due to chance)

10% for all women, 40-70y of age.

And it was below 10%, before the Malmo trial's unexpected upturn. The trial originally reported only 4% risk reduction ratio, which in the course of follow up grew to 19%. No other trial had nearly this magnitude of change in the reported rate. Facts that the trial's autopsy rate simultaneously declined from 3 in 4 to 1 in 3, and that blind to group status death-cause assessment was abandoned in favor of more bias/manipulation-prone open assessment, make the updated data less reliable (another problem with a long-term follow-up is that various forms of uncontrolled or uncontrollable contamination of the originally randomized groups creep in, randomly altering results of statistical analysis).

On the other hand, the four unreliable trials summed up significant, two and a half times higher BC mortality reduction - 25% - for the screened population.

All seven trials add up to 19% reduction over the follow-up period. This figure, however, is not viable in the context of reliability. As all pooled ratios in the review, it was obtained using weighted average concept (Mantel-Haenszel), which is based on trials' size and frequency of the outcome - not their design and execution quality. The 19% weighted average is somewhat higher than the arithmetic average (17.5%), due to more participants and outcomes (BC deaths) in the four inadequate studies, but reliability of data should be more important than mere quantity i.e. study size.

The researchers, Gøtzsche and Nielsen, probably had that in mind, putting out their estimate that what the data suggests is that screening probably reduces BC mortality, and that the

rate of reduction is likely to be about 15%.

This figure is nearly identical to that resulting from another recent independent systematic review of the trial evidence, by the United States Preventive Services Task Force (USPSTF). Based on the same RCTs reviewed by the Nordic Cochrane Center (with Edinburgh also excluded) for the 39-49 age group, it found 15% overall BCM rate reduction. For the 50-59 age group, data from six RCTs (New York excluded, and Age trial had no women 50y and over), the polled BCM reduction rate was 14% (Screening for Breast Cancer: An Update for the U.S. Preventive Services Task Force, Nelson et al. 2009).

Unlike the NCC review, which found most of the trials to be of low quality, the USPSTF review ranked them all as "fair". Thus there was no division on more and less reliable data sources. It is surprising, since among the top USPSTF criteria in evaluating trial quality are

proper randomization and blindness to status in the outcome assessment,

documented to be inadequate or lacking by the NCC in the trials they labeled as inadequate in their analysis - which is listed by the USPSTF among the top evidence resources quality-wise.

Realistically, it is probably more surprising that USPSTF went as far as it did over the line drawn by the overwhelmingly influential pro-screening camp, in setting the mortality reduction benefit due to screening at as "low" as 14-15% level, and by withdrawing its support for the routine screening of women younger than 50. The publication of USPSTF findings was followed by vitriolic reaction from the screening advocates, and its recommendations were rejected.

But, the truth is, the evidence reviewed in the Nordic Cochrane Center (NCC) and USPSTF studies, as incomplete, questionable and not applicable to the population at large, is the best we have. And the indication of BCM reduction benefit due to the screening based on it is probably too optimistic. Literally all these trials took place in the past century, some as far as 4-5 decades ago. Nowadays, with better informed women, higher standards of living, and advance in treatment efficiency, it is likely that the BCM reduction rate due to earlier detection is

lower than what it was decades ago.

But, is that really the best data that we can get from trials? Reasonable objection to these trials in general is the choice of main outcome: breast cancer mortality rate. Not only that the cause-of-death determination has been shown to be plagued with difficulties and bias - it is still only a part of the whole picture. The effect of X-ray mammography screening on the BCM rate is not the most important indicator; it is

the effect on overall mortality rate that should come first.

In other words, somewhat reduced breast cancer mortality cannot be considered beneficial, if it is offset, or even exceeded, by an increased treatment-related mortality from other causes. This rarely addressed, yet crucial question is addressed more closely on next page, for screened vs. unscreened women.